Author response:

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

Public Reviews:

Reviewer #2 (Public review):

In the manuscript Ruhling et al propose a rapid uptake pathway that is dependent on lysosomal exocytosis, lysosomal Ca2+ and acid sphingomyelinase, and further suggest that the intracellular trafficking and fate of the pathogen is dictated by the mode of entry. Overall, this is manuscript argues for an important mechanism of a 'rapid' cellular entry pathway of S.aureus that is dependent on lysosomal exocytosis and acid sphingomyelinase and links the intracellular fate of bacterium including phagosomal dynamics, cytosolic replication and host cell death to different modes of uptake. 

Key strength is the nature of the idea proposed, while continued reliance on inhibitor treatment combined with lack of phenotype / conditional phenotype for genetic knock out is a major weakness. 

In the revised version, the authors perform experiments with ASM KO cells to provide genetic evidence of the role for ASM in S. aureus entry through lysosomal modulation. The key additional experiment is the phenotype of reduced bacterial uptake in low serum, but not in high serum conditions. The authors suggest this could be due to the SM from serum itself affecting the entry. While this explanation is plausible, prolonged exposure of cells to low serum is well documented to alter several cellular functions, particularly in the context of this manuscript, lysosomal positioning, exocytosis and Ca2+ signaling. A better control here could be WT cells grown in low serum.

As the reviewer suggested, we did culture both, WT control cells as well as ASM knock-outs, under low serum conditions before conducting the invasion assays. Hence, the detected effects on S. aureus invasion must be caused by lack of functional ASM in the mutant.

We apologize that this did not become evident from the manuscript’s text. We thus included a change in line 259 which now reads:

”To test whether FBS confounded our invasion experiments, we cultivated WT as well as ASM K.O. cells in medium with reduced FBS concentration (1%) and determined the S. aureus invasion efficiency (Figure 2I).”

If SM in serum can interfere, why do they see such pronounced phenotype on bacterial entry in WT cells upon chemical inhibition?

We explain the differences between inhibitor-treated WT cells and ASM K.O.s by the severe accumulation of SM upon genetic ablation of ASM. We demonstrated this by HPLC-MS/MS measurements in Figure 2L. If cells were cultured in 10% FBS, an ASM K.O. resulted in approx. 4-times higher levels of cellular SM C18:0 when compared to WT cells, while amitriptyline treatment of WT cells had no effect, and ARC39 treatment increased SM C18:0 levels only by 2-fold. This likely results from different durations of SM accumulation in the cell pools which is caused either by complete absence of ASM (in case of the ASM K.O.) or only in the hour-range upon treatment with the inhibitors.

Under low serum conditions, the severe SM C18:0 accumulation in the ASM K.O. was found decreased (from 4-fold to 2-fold when compared to WT cells; Figure 2M). Here, the WT cells used as reference also were cultured in the same manner as the ASM K.O. A similar pattern was observed for other SM species (Supp. Figure 3). This correlates with the S. aureus invasion phenotype in ASM K.O.: under high serum conditions (and resulting in severe SM accumulation) we did not detect an invasion defect, while under low serum conditions (resulting in only moderate SM accumulation) S. aureus invasion was reduced in the knock-outs when compared to WT cells cultured in the same conditions, respectively.

While the authors argue a role for undetectable nano-scale Cer platforms on the cell surface caused by ASM activity, results do not rule out a SM independent role in the cellular uptake phenotype of ASM inhibitors.

Since the comments starting with the line above are identical to the previous comments by the reviewer, we assume that these points of criticism still resound with the Reviewer, although we had agreed previously with the reviewer that we do not show formation of ceramide-enriched platforms, we had changed the manuscript accordingly in the previous revision round already (see also our comment below).

The authors have attempted to address many of the points raised in the previous revision. While the new data presented provide partial evidence, the reliance on chemical inhibitors and lack of clear results directly documenting release of lysosomal Ca2+, or single bacterial tracking, or clear distinction between ASM dependent and independent processes dampen the enthusiasm.

We continue to share the reviewer’s desire to discriminate between ASM-dependent and ASMindependent processes, but the simultaneous occurrence of multiple pathways of bacterial uptake is currently the limiting factor and technological challenge in our laboratory, since these events happen rapidly. We do hope that we or others will be able to address these limitations in the future, for instance with the technologies suggested by the reviewer.

I acknowledge the author's argument of different ASM inhibitors showing similar phenotypes across different assays as pointing to a role for ASM, but the lack of phenotype in ASM KO cells is concerning. The author's argument that altered lipid composition in ASM KO cells could be overcoming the ASMmediated infection effects by other ASM-independent mechanisms is speculative, as they acknowledge, and moderates the importance of ASM-dependent pathway. The SM accumulation in ASM KO cells does not distinguish between localized alterations within the cells. If this pathway can be compensated, how central is it likely to be ? 

We here want to elaborate again, since our revision experiments demonstrate the ASM-dependency of the rapid uptake under low serum conditions – see also above. We were convinced that the genetic evidence of an S. aureus invasion phenotype in ASM K.O.s under these conditions would eliminate the reviewer’s concern about the role of ASM during the bacterial invasion (see also above). Our lipidomics data of ASM K.O.s cultured in 1% and 10% FBS (Figure 2, M, Supp. Figure 3) and inhibitor-treated WT cells (Figure 2L, Supp. Figure 3) show a correlation between SM accumulation and the invasion phenotype observed by us.

We agree with the reviewer, however, that it remains elusive why changes in the sphingolipidome increase ASM-independent S. aureus internalization by host cells. One explanation is a dysfunction of the lipid raft-associated protein caveolin-1 upon strong SM accumulation, which was previously shown to appear in ASM-deficient cells (1, 2). A lack of caveolin-1 results in strongly increased host cell entry of S. aureus in certain cell types (3, 4). In other cell types, such as A549 cells, S. aureus invades in an αtoxin and caveolin-1 dependent fashion (5). It will be interesting to study, to what extent such processes as described by Goldmann and colleagues will depend on ASM. However, a characterization of the mechanism behind these observations requires further experimentation and is beyond the scope of the current manuscript. 

As to the centrality of the pathway: we cannot and do not make any assumptions on the centrality of the pathway and its importance in vivo. As scientists we were intrigued by our finding of an ASM dependent uptake pathway for S. aureus – especially its speed. In different as of yet still unidentified host cell types or cell lines such a pathway may pose a major entry point for pathogens. Alternatively, we may have identified an ASM-dependent mode of receptor uptake, with which the bacteria “piggyback” into the cells.

The authors allude to lower phagosomal escape rate in ASM KO cells compared to inhibitor treatment, which appears to contradict the notion of uptake and intracellular trafficking phenotype being tightly linked. As they point out, these results might be hard to interpret.

We again want to add that we measured phagosomal escape of S. aureus in WT and ASM K.O. cells cultured in 1% FBS (low serum conditions) and compared it to escape rates obtained with host cells cultured in 10% FBS. Again, we infected cells for 10 or 30 min and determined the escape rates 3h p.i. However, the results are similar to escape rates determined with 10% FBS (see Author response image 1). This was addressed already during the manuscript’s first revision. We found that escape rates of S. aureus were significantly decreased in absence of ASM regardless of the FBS concentration in the medium.

Author response image 1.

We therefore think that prolonged absence of ASM has additional side effects. For instance, certain endocytic pathways could be up- or down-regulated to adapt for the absence of ASM or could be affected by other changes in the lipidome (that can be minimized but not completely prevented by culturing cells in 1% FBS). This could, for instance, affect maturation of S. aureus-containing phagosomes and hence phagosomal escape.

As it is currently unclear in how far the prolonged absence of ASM activity affects cellular processes, we think other experiments investigating the role of ASM-dependent invasion for phagosomal escape are more reliable. Most importantly, bacteria that enter host cell early during infection (and thus, predominantly via the “rapid” ASM-dependent pathway) possess lower phagosomal escape rates than bacteria that entered host cells later during infection (Figure 5, D and E). This is confirmed by higher escapes rates upon blocking ASM-dependent invasion with Vacuolin-1 (Figure 4E) and three different ASM inhibitors (Figure 4C and D). We further demonstrate that sphingomyelin on the plasma membrane during invasion influences phagosomal escape, while sphingomyelin levels in the phagosomal membrane did not change phagosomal escape (Figure5 a and b). This is summarized in Figure 5F.

Could an inducible KD system recapitulate (some of) the phenotype of inhibitor treatment? If S. aureus does not escape phagosome in macrophages, could it provide a system to potentially decouple the uptake and intracellular trafficking effects by ASM (or its inhibitor treatment) ?

Knock-downs in our laboratory are based on the vector pLVTHM(6). Inducible knock-downs in the cells would require the introduction of an inducible Tet^on system, which the cells currently do not harbor.

However, it needs to be stated that for optimal gene knock-downs, the induction of this system has to be performed by doxycycline supplementation in the medium for 7 days thus leading to several days of growth of the cells, which will allow the cells to adapt their lipid metabolism thus reflecting a situation that we encounter for the K.O.s.

ASM-dependent uptake of S. aureus in macrophages has been demonstrated before (7). However, the course of infection in macrophages differs from non-professional phagocytes (8). E.g. in macrophages, S. aureus replicates within phagosomes, whereas in non-professional phagocytes replicates in the host cytosol. Absence of ASM therefore may influence the intracellular infection of macrophages with S. aureus in a distinct manner.

The role of ASM on cell surface remains unclear. The hypothesis proposed by the authors that the localized generation of Cer on the surface by released ASM leads to generation of Cer-enriched platforms could be plausible, but is not backed by data, technical challenges to visualize these platforms notwithstanding. These results do not rule out possible SM independent effects of ASM on the cell surface, if indeed the role of ASM is confirmed by controlled genetic depletion studies.

We agree with the reviewer that we do not show generation of ceramide-enriched platforms (see also above). We thus already had changed Figure 6F in the revised manuscript to make clear that it remains elusive whether ceramide-enriched platforms are formed. We also had added a sentence to the discussion (line 615) to emphasize that the existence of these microdomains is still debated in lipid research.

We think that the following observations support SM-dependent effects of ASM during S. aureus invasion:

(i) Reduced invasion upon removing SM from the plasma membrane (Figure 2N, Supp. Figure 2M)

(ii) Increased invasion in TPC1 and Syt7 K.O. (Figure 2, P) in presence of exogenously added SMase.

However, we agree with the reviewer that we do not directly demonstrate ASM-mediated SM cleavage during S. aureus invasion. Hence, we had added a sentence to the discussion that mentions a possible SM-independent role of ASM for invasion (line 556) that reads:

“Since it remains elusive to which extent ASM processes SM on the plasma membrane during S. aureus invasion, one may speculate that ASM could also have functions other than SM metabolization during host cell entry of the pathogen. However, we did not detect a direct interaction between S. aureus and ASM in an S. aureus-host interactome screen (9).”

The reviewer acknowledges technical challenges in directly visualizing lysosomal Ca2+ using the methods outlined. Genetically encoded lysosomal Ca2+ sensor such as Gcamp3-ML1 might provide better ways to directly visualize this during inhibitor treatment, or S. aureus infection. 

We again thank the reviewer for this suggestion. We already had included the following section in our discussion (then: line 593): “Since fluorescent calcium reporters allow to monitor this process microscopically, future experiments may visualize this process in more detail and contribute to our understanding of the underlying signaling. mechanisms.”

References for the purpose of this response letter:

(1) Rappaport, J., C. Garnacho, and S. Muro, Clathrin-mediated endocytosis is impaired in type AB Niemann-Pick disease model cells and can be restored by ICAM-1-mediated enzyme replacement. Mol Pharm, 2014. 11(8): p. 2887-95.

(2) Rappaport, J., et al., Altered Clathrin-Independent Endocytosis in Type A Niemann-Pick Disease Cells and Rescue by ICAM-1-Targeted Enzyme Delivery. Mol Pharm, 2015. 12(5): p. 1366-76.

(3) Hoffmann, C., et al., Caveolin limits membrane microdomain mobility and integrin-mediated uptake of fibronectin-binding pathogens. J Cell Sci, 2010. 123(Pt 24): p. 4280-91.

(4) Tricou, L.-P., et al., Staphylococcus aureus can use an alternative pathway to be internalized by osteoblasts in absence of β1 integrins. Scientific Reports, 2024. 14(1): p. 28643.

(5) Goldmann, O., et al., Alpha-hemolysin promotes internalization of Staphylococcus aureus into human lung epithelial cells via caveolin-1- and cholesterol-rich lipid rafts. Cell Mol Life Sci, 2024. 81(1): p. 435.

(6) Wiznerowicz, M. and D. Trono, Conditional suppression of cellular genes: lentivirus vectormediated drug-inducible RNA interference. J Virol, 2003. 77(16): p. 8957-61.

(7) Li, C., et al., Regulation of Staphylococcus aureus Infection of Macrophages by CD44, Reactive Oxygen Species, and Acid Sphingomyelinase. Antioxid Redox Signal, 2018. 28(10): p. 916-934.

(8) Moldovan, A. and M.J. Fraunholz, In or out: Phagosomal escape of Staphylococcus aureus. Cell Microbiol, 2019. 21(3): p. e12997.

(9) Rühling, M., et al., Identification of the Staphylococcus aureus endothelial cell surface interactome by proximity labeling. mBio, 2025. 0(0): p. e03654-24.

eLife Assessment

This important study shows that the Nora virus, a natural Drosophila pathogen that also persistently infects many laboratory fly stocks, infects intestinal stem cells (ISCs), leading to a shorter life span and increased sensitivity to intestinal infection with the bacterium Pseudomonas. The authors provide convincing data to support their conclusions. The paper provides new insights into virus-host interactions in the Drosophila gut and serves as a warning for scientists who use the fruit fly as a model to study gut physiology.

Reviewer #1 (Public review):

[Editors' note: The article has been improved and several points raised by the reviewers have now been addressed. The authors should ideally further improve the clarity of the figures and the description of the experimental methods. This is particularly important for an article discussing potential confounding factors.]

Summary:

This important article reveals that the Nora virus can colonize the intestinal cells of Drosophila melanogaster, where it persists with minimal immediate impact on its host. However, upon aging, infection, or exposure to toxicants, stem cell activation induces Nora virus proliferation, enabling it to colonize enterocytes. This colonization disrupts enterocyte function, leading to increased gut permeability and a significant reduction in lifespan. Results are convincing and hold significant import for the Drosophila community.

Strengths:

(1) Building on previous studies by Habayeb et al. (2009) and Hanson et al. (2023), this study highlights cryptic Nora virus infection as a crucial factor in aging and gut homeostasis in Drosophila melanogaster.

(2) Consistent with the oral route of Nora virus transmission, the study demonstrates that the virus resides in intestinal stem cells, with its replication directly linked to stem cell proliferation. This process facilitates the colonization of enterocytes, ultimately disrupting intestinal function.

(3) The study establishes a clear connection between stem cell proliferation and virus replication, suggesting that various factors - such as microbiota, aging, diet, and injury - can influence Nora virus dynamics and associated pathology.

(4) The experimental design is robust, comparing infected flies with virus-cured controls to validate findings.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors report that Nora virus, a natural Drosophila pathogen that also persistently infects many laboratory fly stocks, infects intestinal stem cells (ISCs), leading to a shorter life span and increased sensitivity to intestinal infection with the Pseudomonas bacterium. Nora virus infection was associated with an increased proliferation of ISC and disrupted gut barrier function. Genetically, the authors show that increased ISC division in Nora virus and Pseudomonas coinfected flies is driven by signaling through the JAK-STAT pathway and apoptosis.

Accordingly, blocking apoptosis and JAK-STAT signaling reduces viral load, suggesting that in this context the JAK-STAT pathway is proviral in contrast to other previous observations in systemically infected flies. This work adds to the findings of another recent paper showing that another persistent fruit fly virus, Drosophila A virus, also increases ISC proliferation and decreases gut barrier function. Intestinal viruses should therefore be considered confounders in studies of fly intestinal physiology.

Strengths:

Overall, the data are convincing and robust, starting with two wildtype fly stocks (Ore-R strain) that differ in their Nora virus infection status, followed by experiments in which cleared stocks are reinfected with a purified Nora virus stock preparation. The conclusions of the paper will be of interest to scientists working on insect physiology, virology, and immunology, but should also serve as a warning for scientists that use the fly as a model to study gut physiology.

Reviewer #3 (Public review):

Summary:

Franchet et al. sought to characterize the impact of Nora virus on host lifespan and sensitivity to a variety of infectious or stressful treatments. Through careful and rigorous analyses, they provide evidence that the Nora virus greatly impacts fly survival to infection, overall lifespan, and intestinal integrity. The authors have been thorough and rigorous, and the experimental evidence including proper isolation of the virus and Koch's Postulate reinoculation of the organism is excellent. The additional work is valuable and to the gold standard of the field, characterizing the pathology of the gut, including data showing gut leakage, the presence of the virus in the intestinal stem cells, and the importance of stem cell proliferation for virus replication and spread using elegant genetic tools to block stem cell proliferation or enterocyte death.

Strengths:

The authors have been rigorous and careful. The initial finding is presented through the lens of two related strains differing in virus infection. From there, the authors characterized the virus and isolated a purified culture, which they used to reinoculate a cleared strain to demonstrate proper Koch's Postulate satisfaction. The authors have also probed various parameters in terms of dietary importance in relevant conditions for many experiments. The additional work to characterize the pathology of the gut is compelling, using genetic tools to block or allow intestinal stem cell proliferation and enterocyte death through JAK-STAT and JNK signalling alongside the tracing of virus presence using a Nora virus antibody. JAK-STAT and JNK are previously described as regulators of these processes, making these tools appropriate and convincing. It is also interesting to see good evidence that the virus itself is damaging, rather than simply permitting coinfection by gut microbes (which does happen).

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) The study does not explore or discuss how oral ingestion of Nora virus leads to the colonization of stem cells, which are located basally in the gut. This mechanism should be discussed.

We have added an additional paragraph (4th) in the Discussion dealing with this issue and are further discussing the consequences of RNAi potentially not being functional in progenitor cells in the paragraph on antiviral responses.

(2) The authors fail to detect Dicer-GFP fusion protein expression in stem cells, a finding that could explain why the virus persists in these cells. Further investigation is needed to determine whether RNAi functions are effective in stem cells compared to enterocytes. For clarification, the authors could cross esg-Gal4 UAS-GFP and Myo-Gal4 UAS-GFP with UAS GFP-RNAi and/or express a Dicer-GFP construct under a stem cell-specific driver.

Actually, it is well-known in the Drosophila literature on the intestinal epithelium that RNAi functions well in progenitor cells as the technique has been widely used to understand the control of stem cell division and differentiation in tens of articles. We provide here just a few examples: Jiang et al., Nat Commun (2025) https://doi.org/10.1038/s41467-024-55255-1; Zhai et al., PLoS Genetics (2017) https://doi.org/10.1371/journal.pgen.1006854; Wu et al., https://doi.org/10.1371/journal.pgen.1009649.

(3) The presentation of experimental parameters (e.g., pathogen type, temperature, time points) should be improved in the results section and at the top of the figures to enhance clarity. Additionally, details regarding the mode of oral infection (continuous exposure vs. single feeding on a filter) should be specified. Given that fly stock flipping frequency influences microbiota load (as noted in Broderick et al.), this should be reported, especially for lifespan studies.

P. aeruginosa oral infection was always by continuous exposure, as detailed in the Mat.& Meth. section. Nora infection was done by exposure to the viral solution for 24h, as detailed in Mat. & Meth. The flipping frequency had also been reported in that section.

(4) To confirm that enterocyte colonization requires stem cell proliferation and differentiation, the authors should analyze Nora virus localization in JAK-STAT-deficient flies infected with bacteria or toxicants. This would help determine whether the virus can infect enterocytes in the absence of enterocyte differentiation, but stimulation of stem cells.

We now provide these data (pictures and quantification) in Fig.7 G-H and discuss them in the main text.

(5) The study does not discuss the spatial distribution of Nora virus infection along the gut. Specifically, it remains unclear whether viral colonization is higher in gut regions R2 and R3, which contain proliferative stem cells. Addressing this could provide valuable insights into the virus's infection dynamics.

We have now specified that Nora virus was detected only in the posterior midgut; we are now also providing a schematic illustration in Fig. S5J.

Recommendations for the authors:

Major Suggestion

See weaknesses section for key areas requiring improvement.

Minor Suggestions

(1) Line 79: Mention Nox in the text. Key references on Nox include Jones (2013), Iatsenko (2018), and Patel (2016).

Done.

(2) Line 92: The long list of publications is unnecessary and can be shortened.

We are not sure that many investigators are aware of the scope of our studies on host-pathogen relationships and this is the adequate place for a reminder.

(3) Line 196: Cite Choi et al. (Aging Cell, 2008; 7:318-334. doi: 10.1111/j.1474- 9726.2008.00380.x) for the initial work on gut dysplasia during aging. However, note that dysbiosis in aging is demonstrated in Buchon et al. (2009, Genes and Development) and other studies.

Done.

(4) Line 265: It would be interesting to clarify whether the shortened lifespan of Norainfected flies after a clean injury is dependent on the microbiota.

The shortened life span of Nora-infected flies is not due to the injury as demonstrated in Fig. S4F. Hence, the shortened lifespan is differentially affected by the microbiota according to nutrition conditions as documented in Fig. 3D-E.

(5) Line 285: Clarify what is meant by "polyubiquitin promoter"-do the authors mean a ubiquitous Gal4 driver? Specify the Gal4 lines used in the result section.

Done. The construct is a direct fusion of the ubiquitin p63E promoter to the Dicer-fluorescent protein sequences as described in Girardi et al., Sci Rep, 2015.

(6) Line 347: Indicate the references aligning with the most recent studies on this topic.

Done.

(7) Line 373 and elsewhere: Mention studies that have shown the microbiota influence on lifespan, in relation to dietary richness.

Done.

(8) Line 588: Provide details on the method used for hemolymph collection.

Done.

(9) Line 964: Clarify the phrase "as previously shown"-where in this paper was it demonstrated?

The legends have been rewritten and the phrase has been deleted.

(10) Line 987: In "survival of non-infested with PA14," explicitly mention Nora to distinguish between different infections.

Done.

Figures & Experimental Details

(11) Figures: Improve figure legends or add information at the top of figures, specifying:

Number of flies used to monitor Nora virus titer.

Temperature conditions. o Age of flies used in experiments.

Done.

(12) Figure 2E: The lifespan of Nora-negative flies appears very short. Was this lifespan assay conducted at 29{degree sign}C? What was the fly stock flipping rate?

Correct, it was 29°C. As described in the Material and Methods section, the flies were flipped every two (29°C) to four days (25°C).

(13) Figure 4C: Improve labeling on the plate for better clarity.

Done.

(14) Figure 6C: The figure legend on the right is difficult to interpret. Clarify what "+" indicates and explicitly write out the genotype. Is NP identical to NPG4G80?

Done. NP is the NP1 driver. We usually use it in a version that also includes a Gal80^ts transgene to express the gene of interest only at the adult stage.

(15) Dissection Details: Clearly state which part of the gut was dissected-midgut, entire gut, {plus minus} Malpighian tubules. This should be specified in the results section.

Done (no Malpighian tubules nor crop) for RTqPCR analyses.

(16) Clean Injury: Provide more details in the results section regarding the injury site and needle size.

Done.

(17) Use "Abx" instead of "AntiB," as the former is more commonly recognized.

Done.

Reviewer #2 (Public review):

The title does not seem to be fully supported by the data. While the authors convincingly show the increased sensitivity to Pseudomonas infection, effects on another tested bacterium, Serratia marcescens, were not significantly different between Nora-virus-infected and noninfected flies. Thus, effects of 'intestinal infection' seem to be too broad a claim.

We agree with the reviewer and have accordingly modified the title, which now explicitly refers to P. aeruginosa.

Also, whether the Nora virus increases sensitivity to oxidative stress is not so clear to me: the figure that supports this claim is the survival assay of Figure 5F. However, the difference in survival between control and paraquat-treated Nora (-) flies seems to be in the same order as between control and paraquat-treated Nora (+) flies. Rather, cause and effect seem to be the reverse: paraquat increases ISC proliferation, higher viral loads, and consequently shorter survival. I suggest rephrasing the title and conclusions accordingly.

While we usually just directly compare Nora (+) vs. Nora (-) flies with the same conditions, we note that the difference of survival between control and paraquat-treated Nora (-) flies is of about 9 days, based on LT50 values whereas it is of 8 days for Nora(+) flies. This difference is of about two days when comparing Nora (+) to Nora (-) flies exposed to paraquat. Thus, Nora does contribute to an increased sensitivity to oxidative stress likely by the process highlighted by the reviewer and also by its own detrimental action on the homeostasis of the intestinal epithelium and associated disruption of its barrier function.

Quantification of immunofluorescence microscopy is missing, rendering the images somewhat anecdotal. Quantification should be provided. It will then also be of interest to quantify the number of Nora (+) cells, and the Nora virus levels per infected cell (e.g. Figure 5H). Also, the claim that the Nora virus initially infects ISC and later (upon stress) infects enterocytes requires quantification.

Missing quantifications of pictures have been added: Figs. S5E and 7H. We are not sure we understand the reviewer comment on “Nora virus levels per infected cell”: the signal we are seeing may correspond to aggregates of the virus and would be impossible to quantify reliably, e.g., in the right-most panel of Fig. 5H. Fig. 5I clearly shows that no Nora is detected in enterocytes of young 5-day-old flies in the absence of infectious or xenobiotic challenge.

Genetic support for the role of the JAK-STAT pathway in driving ISC proliferation and supporting Nora virus replication is convincing. It would also be of interest to analyze other pathways implicated in ISC proliferation (e.g. JNK, EGFR), especially given the observations of Nigg et al, showing an involvement of STING/NF-kB and EGFR pathway in driving intestinal phenotypes of Drosophila A virus-infected flies (doi: 10.1016/j.cub.2024.05.009).

We agree with the reviewer that these would be interesting experiments to perform, especially in the light of one hypothesis that antiviral defenses may prevent the initial infection of enterocytes as discussed at length in our updated discussion on host antiviral defenses. However, we are currently unable to perform additional experiments and leave it to other interested investigators studying antiviral innate immunity to address these questions. In this work, we used the interference with the JAK-STAT pathway as a second tool to block the division of ISCs.

Figure 5E: An intriguing observation is that GFP:Dicer2 seems to be unstable in Nora virusinfected cells. Here, GFP control driven by the same driver line would be required to confidently conclude that this is due to an effect on Dicer-2 specifically.

Actually, this experiment was not performed using the Gal4-UAS system but a direct fusion. We do know that GFP is stable when expressed in enterocytes, e.g., Lee et al., Cell Host&Microbe (2016) DOI: 10.1016/j.chom.2016.10.010.

Legends are mostly conclusive, and essential information about the experimental setup is missing in the captions of multiple figures, making the interpretation of the data difficult. See my private recommendations for suggestions to improve the data presentation.

Done.

Recommendations for the authors:

Suggestions for the presentation of the data:

(1) I found the names Ore-R(SC) and Ore-R(SM) for noninfected vs infected Ore-R flies not very intuitive. I suggest renaming them into something that makes the infection status clear.

These notations refer to two distinct sub-strains that may reflect different origins with some likely genetic drift accounting for the distinct properties of the two sub-strains. As the ORE-R (SM) have different infection status: infested, cleaned, re-infected, we fear that this would not clarify the matter. Of note, ORE-R(SC) are refractory to Nora virus infection (Fig. S1I).

(2) Please define the number of flies analyzed for survival assays in the legends.

Done.

(3) The authors provide conclusions in most of the figure legends, without providing an explanation of the experiment that was done. Conclusions should be used sparingly, if at all, in legends. Also, relevant information is often missing in the legends (time points after infection, Figure 2E food source, etc.). I suggest the authors carefully double-check their legends and rephrase the conclusive legends with descriptive ones.

Done. The figure legends have been rewritten.

(4) Several of the legends indicate that 'data represent the mean of biological triplicates' however some panels do not represent triplicates (e.g. Figure 1C-E). Please correct.

Done.

(5) Legends: which multiple comparison test was used for ANOVA?

Done. Tukey’s post-hoc test was used for direct comparisons.

(6) Line 888: black arrows are not shown in the figure.

Corrected.

(7) Figure 1F: legend on the figure seems incorrect (all are labeled Nora (+)); likewise for Figure 2C (all labeled Nora (-)).

Corrected.

(8) Materials and methods: please describe how the Nora virus antibody was raised (and specify on line 271 what viral protein is recognized).

Done. As the whole virus was used for immunization, we cannot state which specific viral proteins are detected by the antibody.

(9) Please define what is presented in the box plots (mean, range, whiskers, individual data points).

Done.

(10) Figure 4 and associated text (line 221): a brief explanation of the Smurf assay would be useful.

Done.

(11) Figure 4C: I did not find the picture of the agar plate informative, as similar information is conveyed in Figure 4D. Also, the labelling cannot be clearly read.

Figure 4D provides a quantification of panel C. The readability has been improved.

(12) Figure 4C: It is suggested that Nora-positive, smurf-negative flies were analyzed, but from Figure 4B it seems that these do not exist. Please explain.

The data in Fig. 4B do not represent absolute numbers but percentages. Thus, there were at most 50% of SMURF-positive flies at the time of the assay, the rest being Smurf-negative yet Nora-positive.

(13) The abbreviations PA14 and Db11 are used in several figures. I would suggest defining the abbreviation in the legend to facilitate interpretation.

Done.

(14) Figure 5A/5G: the Nora virus RNA levels in this figure are dramatically lower than the levels in other figure panels. Please check/correct.

Done. The reviewer is indeed correct: we have forgotten to write that for these two panels, the loads are relative and not absolute as is the case in other panels. 5A: the load in whole flies was taken to be 1; 5G: untreated Nora-positive flies were taken to be 1.

(15) Figure 6A: total number of AporTag positive cells are reported. Were the same number of total cells analyzed? Please define.

We have not counted all of the cells in each midgut but provide the number of ApopTag positive cells per midgut. We thus make the assumption that the overall number of midgut cells is not varying much from one midgut to the other. Visual inspection of DAPI-stained nuclei did not reveal any obvious change in the density of enterocyte nuclei as illustrated in Fig. S6 (we guess that everyone in the field is making the same assumption when counting mitotic ISCs with PHH3 staining).

(16) Figure 6C: I find the shades of blue difficult to distinguish and suggest to us other colors.

Done.

(17) There seems to be a large mismatch between the percentage of Nora virus-positive cells in Figures 5C, 6H and the images of Figures 5G and 5H. Why?

We think there might be a mistake with the Figure numbers cited by the referee. We guess the point the referee was trying to raise is the difference of perceived Nora virus burden between Fig. 5H and Fig. 6G, a quite valid point. For Fig. 5H, we had measured the Nora-virus load by RTqPCR (Fig. 5G, relative burden) but had not quantified the images. This is now done and shown in Fig. 5I. In Fig. 5H, young flies were used and hence there was no Nora virus detected in ECs, as now quantified in Fig. 5I. For Fig. 6G, we had to use 30-day old intestines to be able to observe Nora virus in the enterocytes of the controls. We have now included this important point in the main text and in the Figure legends.

(18) The Title of the legend in Figure 7 is not supported by the data as 'spread through the intestine' has not been analyzed. Please adjust.

Done.

(19) All figures in which ANOVA is used: I assume that anything not labeled with an asterisk was found to be non-significant? If so, this should be indicated in the manuscript.

Actually, we have not highlighted obvious differences to maintain clarity (e.g., Fig. 1E between uncured Ore-R(SM) and cured Ore-R(SC). We thus have underlined the biologically relevant differences in the panels. The interested readr can refer to the primary data that are accessible on a data repository.

(20) Figure 7C: the authors may want to contrast their finding that Upd3 was not upregulated in Nora virus-infected flies (in the absence of PA14) with the findings of Kuyateh et al, who did report upregulation of Upd3 (https://doi.org/10.3390/v15091849).

We thank the reviewer for pointing out this study we were unaware of. We would like to point out that this article is difficult to follow as it is not 100% clear in which of the analyzed studies the induction of upd3 was observed and which exact experimental conditions were followed, e.g., young or old flies, whole flies or gut… We have looked in more detail at ref. 133 of this article, which refers to an unpublished study from the Hultmark laboratory that is however available online: (https://www.diva-portal.org/smash/record.jsf?aq2=%5B%5B%5D%5D&c=15&af=%5B%5D&searchType=SIMPLE&sortOrder2=title_sort_asc&query=Nora+virus&language=en&pid=diva2%3A1045375&aq=%5B%5B%5D%5D&sf=all&aqe=%5B%5D&sortOrder=author_sort_asc&onlyFullText=false&noOfRows=50&dswid=4587).

In that study, flies were “infected” with Nora virus by expressing a cDNA clone injected into embryos. The problem is that for some unknown reasons the authors used Relish mutant flies. It is thus difficult to conclude as these flies are defective for the IMD and Sting pathways whereas our flies are wild-type. We were also interested to read that genes involved in midgut stem cells differentiation were expressed in flies harboring Nora virus, which is in keeping with the data of the present study. However, it is difficult to discuss this when we know little on the background of the studies analyzed by Kuyateh et al, in as much as our Discussion is already rather long.

(21) Figure 7E: are the differences between control and Dome/Stat knockdown flies significantly different for Nora (+) flies (in the absence of Pseudomonas)? This is not clear from the data presentation.

The answer to the question is positive: the JAK-STAT pathway also contributes to the maintenance of intestinal epithelium homeostasis in the absence of bacterial infection, that is presumably basal conditions. We have modified Fig. 7E to include more comparisons.

Textual suggestions:

(22) Line 25 strives > thrives

Done.

(23) Lines 150- 152, etc are not very informative. Also, some of the viruses analyzed are not "known contaminating viruses", but viruses used experimentally (VSV, IIV6, CrPV). I suggest adjusting the phrasing.

Done.

(24) Line 862: weaker fitness > lower fitness.

Done.

(25) Virology terms:

(a) I suggest not using the term titer for qPCR readouts (which do not involve titration). Viral RNA level or viral RNA load would be more appropriate.

Done.

(b) I would propose rephrasing the Y-axis label of Figure 1C, E to Nora RNA load (same for other figures showing viral RNA).

Done.

(c) Infested: rather use the more accurate term infected.

Done.

(d) Contamination: rather use the term infection.

We have modified some but not all occurrences of this word. We believe that it is important to use the word contamination when referring to enterocytes: the enterocytes are not infected by Nora; rather, differentiated infected ISCs become contaminated enterocytes. Infection refers to an active process whereas contamination refers to a state.

(e) Proliferation: rather use the term replication.

According to our US-English dictionary, proliferation refers to the “rapid reproduction of a cell, part, or organism”, which is the meaning we intend. Replication does not have this notion of speed of reproduction.

(f) Drosophila should not be italicized in Drosophila A virus, following the ICTV convention that a "virus name should never be italicized, even when it includes the name of a host species or genus" https://ictv.global/faq/names.

Done.

(26) Line 873-975: please rephrase the legend of Figure 1F as the current one is not informative.

Done.

(27) Line 934: I suggest moving the justification of the time point chosen "= LT50 on the survival test in 935 Fig. 2E" to the main text.

Done.

(28) Line 936: with drop > with a drop.

No longer relevant.

(29) Line 940-941: the grammar of the sentence does not seem to be correct as it suggests that SDS induces Diptericin expression.

No longer relevant.

(30) Line 952-953; line 980: please correct mismatch singular/plural (antibody have, inhibition do).

Done.

(31) Line 422: "It will be interesting to determine whether the absence of a Dcr2 fluorescent proteins fusions in progenitor cells that we report in this study rules out a role for the RNAi pathway in intestinal host defense against the Nora virus". It would be of interest to discuss this finding in the context that virus-derived Nora virus siRNAs can be easily detected and that the viruses encode an RNAi antagonist (doi: 10.1371/journal.ppat.1002872).

Done. We have updated the Discussion and propose a model whereby RNAi would prevent primary infection of enterocytes and then virus replication in proliferating progenitor cells would allow the virus to effectively inhibit the RNAi machinery when the infected progenitor cells become enterocytes.

(32) Line 159: Nora virus phenotypes differ between laboratories. I would be interested to read the authors' speculations on why this would be the case.

Our work shows that the effects of Nora virus depend significantly on several parameters we have identified: nutrition quality, age, exposure to abiotic or biotic stresses, and fly genotypes with the existence of Nora-refractory strains. These parameters as well as potential differences between laboratories are actually discussed in the second paragraph of the Discussion.

(32) Line 175: capitalization of ORE-R vs Ore-R at other places in the manuscript.

Done.

(33) Line 185-194: PA14 and Pseudomonas are used interchangeably. Perhaps it is clearer to stick to a single term for consistency.

PA14 is one clinical strain used to study P. aeruginosa. There are many others such as PAO1, which is also widely used. We have decided to write P. aeruginosa PA14 the first time we are using it in each figure legend, and use only PA14 afterwards.

Reviewer #3 (Public review):

The claim that Dcr2 is not abundant in ISCs because the protein is not stable is logically consistent and reasonable. Perhaps I missed this, but the authors could additionally knock down or use somatic CRISPR to delete Dcr2 in ISCs to test whether a lack of Dcr2 underlies sensitivity. In this experiment, the expectation would be that depleting Dcr2 in ISCs genetically would make little difference to susceptibility overall compared to controls. This is not an essential experiment request.

We agree with the reviewer that these would be interesting experiments to perform. However, we are currently unable to perform additional experiments and leave it to other interested investigators studying antiviral innate immunity to address these questions dealing with the specific steps of RNA interference that may be missing in progenitor cells.

Recommendations for the authors:

(1) Line 206-207 and 214-216: the order of ideas presented here is unintuitive. In Lines 206207, it is said that ABX treatment had no effect, which is counterintuitive to the nature of infection susceptibility. But this is resolved in Lines 214-216 when the reader realizes that S3G is fed on a sucrose solution, and so likely microbiota-depleted. Perhaps more could be said to clarify this in the main text, and/or swap the order of these observations so a casual reader is not confused about the nature and extent of the microbiota contributing to the sensitivity of Nora-infected flies.

As suggested by the reviewer, we have clarified the text with respect to the food source and microbiota load; we emphasize that the microbiota plays a protective role in Nora-negative flies fed on sucrose solution even though the microbiota load is very low under these conditions. Of note, the microbiota is not depleted in sucrose-fed Nora-positive flies: we suspect that delaminating enterocytes may actually provide directly or more likely indirectly (peritrophic matrix) nutrients for the microbiota.

(2) Line 262-265: the text may be a bit exaggerated given only 3 pathogens tested, one of which was a fungal natural infection breaching the cuticle and largely bypassing the gut. This could be re-phrased.

The important point is that uninfected Nora-positive flies die with a LT50 of about 10 days even when noninfected; it has nothing to do with the number of pathogens tested. Thus, any infection that causes death with kinetics in this range may be misinterpreted in the absence of a relevant uninjured or clean injury control.

(3) Line 379-382: I don't know if citing Schissel et al. is needed here. This paper's methods and data are highly problematic, as mentioned by the authors. This is not a highly cited paper, nor does it add value to the present discussion to cite it only to discredit it. Perhaps this can be left out and the field can move on quietly - naturally, this choice is the present authors', and this is just my view.

We have actually cited this article at two other places and thus had not cited it “only to discredit it”. We have nevertheless removed the lines as suggested by the reviewer.

(4) Line 404: perhaps clarify "Interestingly, mammalian stem cells..."

Done.

(5) Line 455: my understanding of digital PCR is that it is highly useful for detecting rare variants but not particularly better than qPCR for estimating loads/titres? This is not to say dPCR is worse, just that dPCR and primer-specific RT + qPCR are comparable if load/titre is desired. For instance, Qiagen actually recommends qPCR over dPCR specifically (and pretty much exclusively) for gene expression: https://www.qiagen.com/us/applications/digitalpcr/beginners/dpcr-vs-qpcr.

(6) Perhaps Line 455 could drop the advocacy for digital PCR? I agree using dissected guts, or seemingly aged individuals per Figure 3B(?), is a valuable thing to point out. Maybe the aged individuals point could be added here? I guess the idea behind dissected guts is to have samples enriched in Nora virus.

Cleaning Nora-positive strains is really difficult and we suspect that as long as there is one viral particle left, it may be sufficient to re-ignite the contamination of the strain. Our own experience with digital PCR on the expression of AMP-like molecules in the head of flies is that we found the approach to be more sensitive than classical RTqPCR (Xu et al., EMBO Rep, 2023).

eLife Assessment

This valuable study identifies and characterizes probe binding errors in a widely used commercial platform for spatial transcriptomics, discovering that at least 21 out of 280 genes in a human breast cancer panel are not accurately detected. The authors provide convincing evidence for their findings through validation against multiple independent sequencing technologies and reference datasets, and they introduce a computational tool to help predict potential off-target probe binding. Given the broad adoption of this platform in biomedical research, this work provides an essential quality control resource that will improve data interpretation across numerous studies.

Reviewer #2 (Public review):

This paper describes an analysis of a commercially available panel for a spatial transcriptomic approach and introduces a computational tool to predict potential off-target binding sites for the type of probe used in the aforementioned panel. The performance of the prediction tool was validated by examining a dataset that profiled the same cancer tissue with multiple modalities. Finally, a detailed analysis of the potential pitfalls in a published study communicated by the company that commercialized the spatial transcriptomic platform in question is provided, along with best practice guidelines for future studies to follow.

Strengths:

- The manuscript is clearly written and easy to follow.<br /> - The authors provide clean, organized, and well-documented code in the associated GitHub repository.

Comments on revision:

My impressions from the first round of review haven't really changed. I don't think the software tool is well developed, and failing to incorporate thermodynamics or consider the impact of alignment settings is a major weakness.

I do think the topical area is relevant. The inclusion of the Xenium /Hubmap data modestly strengthens the manuscript relative to the original submission.

Reviewer #3 (Public review):

Summary:

The authors present a new computational method (OPT) for predicting off-target probe binding in the commercial 10X Xenium spatial transcriptomics platform. They identified 28 genes in the 10x xenium human breast cancer gene panel (280 genes) that are not accurately detected at the single-molecule level. They validated the predicted off-target binding using reference data from single-cell RNA-seq and 3'-sequencing-based Visium RNA-seq. This work provides a practical resource and will serve as a valuable reference for future data interpretation.

Strengths:

(1) Provides a toolbox for the community to identify off-target probes.

(2) Validates the predictions using single-cell RNA-seq and sequencing-based Visium RNA-seq datasets.

Comments on revision:

The authors state that OPT is a new software tool and have posted example code on GitHub. However, the Jupyter notebook does not display any figures or workflows that would allow the process to be replicated. Please provide documentation and code that can reproduce the results/figures presented in the paper.

Author Response:

The following is the authors’ response to the original reviews

Public Reviews:

We thank the editors and the reviewers for their constructive feedback in helping us strengthen this manuscript.

During the revision process, new information was shared with us by the 10x Genomics team regarding the Xenium probe sequences evaluated in our original paper. Briefly, the Xenium probe sequences we evaluated represented an earlier iteration of the probes used to generate the data in Janesick et al. Further, we were made aware that the probe sequences used in Janesick et al. represented an earlier iteration of the commercially available Xenium v1 Human Breast Gene Expression Panel. We now elaborate further in a new Supplementary Note. We have therefore updated the paper throughout to reflect this new understanding, though we emphasize that our conclusions do not change. Rather, this newfound understanding provides stronger evidence of off-target probe binding with imperfect sequence matching, which we support with new supplementary figures.

(1) Limited evaluation of tissues and gene panels

“The results were only tested with one tissue (human breast). However, this is not a major weakness, as one can easily extrapolate that this should be the case for any other tissue.”

“Does not apply the OPT method to the most widely used Xenium gene panels (e.g., pan-Human, pan-Mouse panels with ~5,000 genes each).”

“The authors claim that OPT is a generalizable method for identifying off-target probes. To support this claim, they should provide similar predictions for the Xenium Pan-Human or Pan-Mouse gene panels, which are more widely used than the breast cancer panel.”

“While I understand that conducting new experimental studies is likely beyond the authors' intended scope of the manuscript, the narrow reliance on Janesick et al. for all of the validation makes it difficult to assess the broad usability of OPT. In the absence of designing and then validating novel padlock probe designs with OPT, are there other publicly available datasets that authors could perform secondary analysis on using OPT?”

Our primary focus on breast cancer was driven by data availability rather than tissue specificity. For this probe panel, matched Xenium, Visium, and scRNA-seq datasets are publicly available, enabling direct cross-platform comparisons of gene expression and allowing us to evaluate the impact of off-target probe binding in Xenium.

OPT is tissue-agnostic and can be applied to any probe panel regardless of tissue type. To demonstrate this generalizability, we have now applied OPT on all publicly available 10x Genomics probe sets beyond the breast panel, including the Xenium pan-Human and pan-Mouse gene panels. The complete results of these analyses have been generated and are provided as a compressed zip file accompanying the revised manuscript.

Beyond pre-designed panels, in this revision, we have now also applied OPT to custom Xenium gene panels from the Human BioMolecular Atlas Program (HUBMAP) and further demonstrate integration of HUBMAP RNA-seq data to evaluate the impact of potential predicted off-targets in a new section “Bulk RNA-seq reference atlases suggest off-target binding can variably impact results in Xenium custom probe panels.”

Overall, in these newly evaluated panels, we identify many cases of off-target probe binding with non-negligible expression of off-target genes in the target tissue, underscoring that our findings are not specific to human breast tissue. Therefore, in the revision, we have broadened the title to “Evidence of off-target probe binding affecting 10x Genomics Xenium Gene Panels compromise accuracy of spatial transcriptomic profiling”

(2) Limited quantifications

“Lacks clarity on how the confidence level of off-target predictions is calculated.”

“How can the confidence level of these off-target predictions be quantitatively assessed? Please provide benchmarks or validation metrics if available.”

We thank the reviewer for raising this important point. To strengthen our claim that predicted off-targets can contribute to observed Xenium expression patterns, we incorporated a quantitative assessment in addition to the qualitative comparisons presented previously. Specifically, we leveraged Visium and scRNA-seq data to compare spot- and cluster-level expression of target genes alone versus expression aggregated with their predicted off-target genes. Across all examples shown, inclusion of predicted off-targets consistently resulted in stronger agreement with the Xenium results, as reflected by decreased RMSE and increased Pearson correlation relative to using the target gene alone.

We emphasize, however, that OPT does not assign a formal confidence score to off-target predictions based on sequencing data alone. Importantly, identification of a potential off-target by OPT does not imply that it will necessarily affect Xenium results. As we’ve noted, if the off-target gene is not expressed, then it will not affect the observed gene expression magnitudes of the target gene. To help users assess whether predicted off-target genes will affect observed gene expression magnitudes of the target gene for a tissue of interest, we now provide a complementary analysis, including heat-map visualizations comparing the expression of target genes and their predicted off-targets in matched bulk RNA-seq or scRNA-seq datasets from the same tissue (Supplementary Figures 9, 10, 11). We hope this evaluation pipeline will clarify to researchers they can evaluate whether predicted off-targets will appreciably affect results in their tissue of interest.

(3) Under-developed and non-essential software

“The manuscript section on the software tool feels underdeveloped.”

“Once the 10X Genomics corrects their gene panels according to this finding, the tool (OPT) will not be useful for most people. Still, it can be used by those who want to design de novo probes from scratch.”

“Since the authors claim that OPT is intended for community use, the paper should provide a clear, step-by-step user guide, such as Jupyter tutorial, ideally as supplementary material.”

We agree with the reviewers that the description of the software tool itself is relatively concise. This is intentional, as the primary goal of this manuscript is not to introduce a standalone software framework, but rather to use the tool as a means to characterize and quantify off-target probe binding and its potential downstream impact on spatial gene expression analyses. Accordingly, our emphasis is placed on the biological and analytical insights enabled by this approach, rather than on extensive software tool details. To support potential users, we have now included additional software documented with an example Python notebook demonstrating how it can be applied to any probe panels in the GitHub repository: https://github.com/JEFworks-Lab/off-target-probe-tracker/blob/main/example.ipynb

Likewise, the primary goal of this manuscript is not to suggest that a specific vendor’s probe panels are flawed, but rather to demonstrate that off-target probe binding is a general and underappreciated phenomenon that can occur in some probe-based spatial transcriptomics platforms to meaningfully impact downstream analyses and biological interpretation.

OPT was developed as a framework to identify potential off-target probe interactions based on sequence homology. In practice, OPT can serve as a post hoc tool that allows researchers to assess whether predicted off-target interactions may exist in a given panel and to account for these possibilities when interpreting spatial expression patterns, even when panels have been developed by the many probe designing methods now highlighted in the revised manuscript. Given the complexity of probe design and hybridization behavior, we believe that explicitly identifying and reporting potential off-targets remains valuable for downstream data interpretation, cross platform comparisons, and reproducibility. Thus, OPT is intended to complement existing probe design strategies and vendor efforts, rather than replace them, by providing researchers with additional context to interpret their data more accurately.

In our revision, we have therefore elaborated on this in the discussion, reiterated here for convenience: “Although we focus here on the 10x Genomics Xenium technology, we do not exclude the possibility that off-target binding may similarly affect other probe-based gene detection approaches from other commercial vendors. Any technology that relies on hybridization-based detection is inherently susceptible to off-target probe binding when sequence similarity exists. Further, hybridization-based detection often inherently involves a trade-off between sensitivity and specificity. Given these inherent technological limitations, we therefore emphasize the importance of transparency through sharing probe sequences. However, many companies do not release the probe sequences used in their assays, limiting the consumer’s ability to fully interpret their results as well as the community’s ability to effectively characterize and benchmark performance variation across platforms. Therefore, we strongly recommend that companies publish probe sequences for pre-designed panels and likewise that researchers using these technologies should obtain and publish probe sequences used in their studies to support transparent and reproducible science. “

Recommendations for the authors:

“The paper only describes evidence of the off-target effect based on perfect sequence homology, although the tool (OPT) provides an option to find additional "potential" off-targets that allow mismatches. It would be very nice if the authors could additionally provide at least one example of off-target binding with at least one mismatch.”

We thank the reviewer for the opportunity to clarify this point. In addition to analyses based on perfect sequence homology, we examined predicted off-target binding when allowing mismatches at the terminal ends of probe sequences. This analysis is presented in the Results section titled “OPT results when allowing mismatches at the terminal ends of the probe sequences identifies additional off-target candidates.”

In this revision, we now allowed a 10bp padding on either end of the 40bp probe sequence, permitting imperfect sequence matching at the terminal regions. Under these conditions, OPT identified additional off-target candidates, including TUBB2B and ACTG2, which we highlight as representative examples (Supplementary 7,8). We further demonstrate how these predicted off-target interactions impact gene expression concordance by comparing Xenium measurements with both Visium and scRNA-seq data, showing measurable changes in cross-platform agreement. Together, these results illustrate that allowing mismatches reveals biologically relevant off-target effects beyond those captured by perfect sequence homology alone.

“Clarifications and updates for Figure 2A-B

Xenium offers a resolution of up to 200 nanometers with continuous readout, without pixel gaps. However, the figures shown in Figure 2A-B appear pixelated - why is this the case? Could the authors clarify this discrepancy and, if possible, provide the raw feature intensity data for Xenium in the supplementary materials?

Additionally, there appear to be no visible gaps in the Visium graphs. Could the authors update the figure panels to represent the true spot locations for Visium, to more accurately reflect the underlying data structure?”

We thank the reviewer for the opportunity to clarify these points. The goal of Figure 2A-B is to facilitate a direct visual comparison of gene expression patterns between the Visium and Xenium platforms. To enable this comparison, we aggregated the single-cell Xenium data into spatial patches matching the effective resolution of Visium spots (55x55µm). Similarly, Visium spots were rendered as patches to produce a more continuous visual representation. As a result of this aggregation and visualization choice, the Xenium expression plots appear pixelated despite Xenium’s native subcellular resolution (up to ~200 nm with continuous readout). We have clarified this processing and visualization step in the Methods to avoid confusion.

With respect to the Visium expression plots, the lack of gaps is also a consequence of rendering each spot as a filled patch rather than plotting traditional Visium spots. This was done intentionally to maintain visual consistency with the aggregated Xenium data and to emphasize spatial concordance rather than the underlying sampling geometry. We have now explicitly stated this design choice to improve clarity.

“I found the format of the manuscript to be at times confusing and perhaps a bit of an odd fit for a general interest journal. A significant portion of the manuscript is spent critiquing a specific publication, "High resolution mapping of the tumor microenvironment using integrated single-cell, spatial and in situ analysis" published by Janesick et al. (of 10x Genomics, Inc.) in Nature Communications in 2023. This content would seem more appropriate as a Comment submitted to Nature Communications, potentially to be accompanied by a response from the authors of Janesick et al. at 10x.”

I would like to address this important point as the corresponding author who takes primary responsibility for the unconventional decision to submit this manuscript to eLife as opposed to as a commentary suggested by the reviewer.

Consistent with the reviewer, I did initially consider submitting this as a Matters Arising to Nature Communications. However, after consultation with other senior colleagues and co-authors, I decided to forgo this route on the basis that the information provided in a Matters Arising must be kept confidential. I was concerned that this would lead to long, drawn-out private exchanges. As we note in the manuscript, the Xenium platform's widespread use and high cost imposed a certain urgency that I believed warranted open and rapid dissemination.

Therefore, we submitted to eLife with the hope that eLife’s unique continuous post-publication public peer review process will enable the rapid dissemination of these important financially-sensitive insights while permitting constructive criticisms from both industry and academic expert reviewers to be openly considered by all readers.

eLife Assessment

This important study developed a novel paradigm combined with EEG recordings to examine the neural mechanisms underlying temporal integration in perception and its modulation by prior history (i.e., the serial dependence effect). The results provide solid evidence that two key EEG features, namely the individual alpha frequency and the aperiodic slope, jointly and independently shape perceptual integration and its reliance on prior information. While additional control analyses would further strengthen the main conclusions, the findings will be of broad interest to researchers studying perception, decision-making, inter-individual differences, and brain rhythms.

Reviewer #1 (Public review):

Summary

Alpha oscillations have been previously proposed to shape the temporal resolution of visual perception, with a higher alpha frequency providing a finer resolution. This study goes beyond by investigating three additional processes that could influence joint visual temporal perception: the aperiodic neural signal, the integration of recent perceptual experience (serial dependence), and subjective confidence. To address their question, they developed a novel task where two Gabor patches oriented in opposite directions are presented in a continuous stream. This allows for testing for robust perceptual integration while avoiding bias from suboptimal perception. Behavioral analyses revealed an association between confidence and individual temporal integration thresholds, and demonstrated that serial dependence biases visual temporal integration as well as its associated confidence. EEG analyses first replicated the previous findings showing that faster IAF provides higher temporal resolution. Interestingly, the aperiodic neural signal was associated with both perceptual and temporal precision. Finally, the authors show that serial dependence is reduced in individuals with faster IAF and enhanced in participants exhibiting a stronger aperiodic component. Together, these findings highlighted that visual temporal integration arises from an interplay between alpha oscillations, the aperiodic signal, serial dependance and subjective confidence.

Strengths:

(1) The novel task proposed in the study represents a substantial improvement over the two-flash fusion task previously used to investigate the role of alpha oscillations in visual temporal perception.

(2) Serial dependence has attracted increasing interest in vision research in recent years. Testing whether recent visual inputs also influence temporal resolution is, therefore, a valuable and timely approach. In this regard, the authors provide evidence for a serial dependence effect.

(3) Although the functional role of brain oscillations has been extensively studied over the past decade, the role of the aperiodic neural signal has long been overlooked. This study revealed that the aperiodic component plays a role in perceptual precision and temporal resolution, thus providing evidence for an important role of the aperiodic neural signal.

(4) The mediation analysis demonstrates that the aperiodic and oscillatory neural components act independently, providing important insights for future studies aimed at understanding their respective role.

Weaknesses

It would have been valuable to record EEG continuously during the experiment to investigate how spontaneous alpha oscillations and aperiodic signal dynamically influence the temporal integration, serial dependance and confidence on a trial-by-trial basis.

Appraisal

The authors employed a novel and thoughtfully designed task, combined with appropriate analyses, to address their research question. Their results are convincing and provide strong support for their conclusions.

Impact

This study provides valuable insights into the role of the aperiodic neural signal in visual temporal integration. This is important because its contribution has likely been underestimated, and future research will likely uncover increasing evidence of its impact across multiple cognitive functions.

It was also very interesting to observe how alpha oscillations are associated with serial dependence and confidence, extending beyond their well-known role in visual temporal resolution. This opens intriguing avenues for future research on the functional role of alpha oscillations.

Reviewer #2 (Public review):

Summary:

This paper examines resting-state electroencephalography (EEG), the electrophysiological underpinnings of the temporal integration window in perception, and its modulation by priors (serial dependence) as measured through the perceptual fusion point of two continuous alternating stimuli. The study also includes a measure of perceptual confidence. Separating periodic from aperiodic EEG activity, the results show that the faster the individual alpha-frequency at rest and the steeper the aperiodic slope (previously linked to higher sampling/ lower noise), the lower the perceptual fusion point (corresponding to narrower integration windows), with independent contributions of the period and aperiodic activity to the integration window. The data also reveal that the point of fusion depends on prior history, and that the strength of this effect depends on individual alpha frequency and aperiodic slope: the lower the individual alpha frequency and the aperiodic slope, the stronger the serial dependence, with the two contributions being again independent. Higher alpha frequency also led to higher confidence. The results are interpreted to suggest that speed of alpha oscillations and aperiodic slope of the power spectrum (presumably reflecting rate/fidelity of visual sampling and the level of background noise) jointly shape the perceptual measure under study: high rate/ fidelity and low noise promote temporal precision in integration, while lower rate/fidelity and higher noise lead to a higher reliance on prior history. It is concluded that it is the interaction between two EEG features that shapes temporal integration and hence perceptual fusion.

Strengths:

The strength lies in the use of a continuous visual stream of two alternating stimuli whose timing shapes fusion or separation of the two stimulus precepts, avoiding some of the pitfalls of previous fusion probes through discrete (not continuous) stimulus pairs (missed detection of one stimulus of the pair may be misinterpreted as fusion). The results seem robust (based on n=83 participants), the results are interesting, and the interpretations are sound.

Weaknesses:

The main weakness lies in the reliance on resting state EEG for correlation with the behavioural measures. This captures trait-based relationships, but does miss out on the brain activity dynamics within/across trials, which could be used for a direct readout of evidence accumulation to a decision, for capturing spontaneous fluctuations of the processes under study, etc. Also, in terms of resting state EEG, both eyes-closed (EC) and eyes-open (EO) data have been recorded, but their links to perceptual fusion point/ confidence seem somewhat inconsistent across the results. This is a bit confusing. Are the EO and EC signals in any way related/ correlated, and if not, what are they supposed to represent? Would an analysis of these EEG measures during task performance (e.g., in a pre-stimulus = baseline time window) provide more consistent results? These points could be resolved by additional analyses and/or more elaborate discussions.

Reviewer #3 (Public review):

Summary:

In this study, the authors seek to explain what influences the temporal resolution of visual perception and its associated metacognitive monitoring, interindividual differences in such processes, and the neural mechanisms associated with these interindividual differences. More specifically, they investigated the factors influencing the perception of a rapid alternating stream of visual patterns as a single fused percept versus two segregated stimuli, and how these factors relate to stable features of ongoing brain activity. They introduce a novel sustained-stream temporal integration paradigm designed to address limitations of traditional two-flash tasks, and combine this with resting-state electroencephalography (EEG) to examine how individual alpha peak frequency and the aperiodic component of the power spectrum relate to temporal integration thresholds, perceptual history effects, and subjective confidence. Their overarching aim is to move beyond a purely oscillatory account of temporal sampling and to test whether periodic (alpha) and non-periodic (aperiodic) neural dynamics jointly shape perceptual decisions.

Strengths:

The study has several notable strengths. First, the experimental paradigm represents a thoughtful and innovative refinement of earlier approaches. By presenting alternating gratings within a continuous stream and varying the duration of each element rather than introducing discrete blank intervals, the authors mitigate well-known confounds of classical two-flash paradigms, particularly the possibility that "fusion" reports reflect missed detections rather than genuine temporal integration. The psychometric functions are well characterized, and the sample size is large for an individual-differences EEG study, with an a priori power analysis supporting the adequacy of the sample. Second, the use of spectral parameterization to separate oscillatory alpha peak frequency from the aperiodic component of the spectrum is methodologically rigorous and timely, as this distinction is increasingly recognized as important to avoid confounds in oscillatory activity estimation and the measurement of neural noise/excitatory-inhibitory balance (i.e., the aperiodic component of the power spectrum). The present work contributes to this emerging direction by relating both to behavioral indices within the same dataset. Third, the integration of perceptual thresholds, serial dependence, and subjective confidence within a unified framework provides a richer account of temporal perception than studies focusing on a single measure. In particular, the demonstration that resting alpha frequency predicts integration thresholds and that the aperiodic exponent relates to variability of the psychometric function is broadly consistent with the authors' central claims.

Weaknesses:

(1) At the same time, several aspects of the interpretation require caution. One conceptual issue concerns the interpretation of the psychometric slope parameter as an index of "temporal precision." The manuscript consistently equates steeper slopes with higher perceptual precision or lower internal noise. However, the slope of a binary psychometric function does not uniquely index sensory temporal resolution. It reflects the steepness of the transition between response categories and can arise from multiple sources, including variability in sensory encoding, instability of decision criteria, lapse rates, or other decisional processes. Even in the literature cited by the authors, slope is often described more generally as reflecting perceptual variability or sensory and/or decision noise rather than a pure measure of perceptual precision. An abrupt transition from "fused" to "segregated" responses, therefore, does not necessarily imply finer temporal resolution at the sensory level; it may instead reflect more consistent categorization or reduced decisional variability. The present data convincingly demonstrate relationships between spectral measures and the steepness of behavioral transitions, but they do not by themselves establish that this steepness reflects perceptual temporal precision rather than broader sources of behavioral variability.

(2) A related concern involves the causal language used to describe the relationship between neural measures and behavior. The EEG metrics are derived from resting-state recordings and therefore reflect stable, trait-like individual differences. Nonetheless, the Discussion sometimes adopts mechanistic phrasing suggesting that slower alpha rhythms or flatter spectra lead the brain to compensate by weighting prior information more heavily, or that neural noise is being "regulated." Such formulations imply within-task adaptive processes that are not directly measured. The results demonstrate robust between-participant associations, but further research is needed to establish whether individuals regulate neural noise or adjust prior weighting dynamically.

(3) Another point that merits clarification concerns the control analyses. The authors appropriately use spectral parameterization to dissociate oscillatory alpha peak frequency from the aperiodic component in the main analyses; however, their subsequent control analyses examining other frequency bands appear to rely on conventional band-power measures. Because band power can be influenced by the aperiodic background, null effects in other bands are difficult to interpret without similarly accounting for aperiodic structure.

(4) In addition, the temporal structure of the stimulus stream introduces an interpretational nuance. Varying the duration of each Gabor in a continuous alternation produces quasi-periodic stimulation rates, and several of these ISIs fall within the alpha frequency range. Rhythmic visual stimulation at alpha-range frequencies is known to produce strong stimulus-locked responses and can interact with intrinsic alpha rhythms in a frequency-dependent manner (Keitel et al., 2019; Gulbinaite et al., 2017). Although the present study does not record EEG during task performance and therefore cannot directly assess stimulus-driven steady-state responses, this aspect of the design complicates a purely intrinsic sampling interpretation. The observed relationship between resting alpha frequency and integration thresholds may reflect intrinsic sampling speed, but it could also be influenced by how closely an individual's alpha rhythm aligns with alpha-range temporal structure in the stimulus.

Conclusion:

Despite these limitations, the study achieves many of its primary aims. The sustained-stream paradigm reliably elicits graded temporal integration behavior and robust serial dependence effects. Individual alpha frequency is convincingly associated with integration thresholds, and the aperiodic exponent relates to behavioral variability measures. These findings support the broader conclusion that temporal perception reflects an interaction between rhythmic neural dynamics and the background spectral structure of ongoing activity. The work is likely to have a meaningful impact for researchers studying perceptual timing, perceptual history, individual differences in brain rhythms, and the functional role of aperiodic neural activity.

References:

Keitel, C., Keitel, A., Benwell, C. S., Daube, C., Thut, G., & Gross, J. (2019). Stimulus-driven brain rhythms within the alpha band: The attentional-modulation conundrum. Journal of Neuroscience, 39(16), 3119-3129.

Gulbinaite, R., Van Viegen, T., Wieling, M., Cohen, M. X., & VanRullen, R. (2017). Individual alpha peak frequency predicts 10 Hz flicker effects on selective attention. Journal of Neuroscience, 37(42), 10173-10184.

Author Response:

(1) Clarification of the distinction between resting-state trait measures and ongoing neural dynamics

All the Reviewers commented that this study provides a useful characterization of the relationship between trait-based resting-state neural dynamics and behavioral measures. At the same time, we agree that including ongoing EEG dynamics during task performance would have added important complementary information. In particular, task-related EEG would allow a more direct characterization of the relationship between ongoing neural activity and behavioral indices at the single trial level, thereby helping to clarify the role of ongoing neural dynamics in evidence accumulation and perceptual decision-making. It would also enable testing how pre-stimulus alpha oscillations and aperiodic activity dynamically influence temporal integration, serial dependence, and confidence on a trial-by-trial basis.

However, we would like to emphasize that the primary aim of the present study was to investigate trait-level resting-state neural dynamics, which are known to be relatively stable and consistent within individuals, such as individual alpha frequency (e.g., Grandy et al., 2013; Wiesman & Wilson, 2019; Gray & Emmanouil, 2020) and aperiodic neural dynamics (Demuru and Fraschini, 2020; Pathania et al., 2021; Euler et al., 2024), and to examine whether these stable neural characteristics predict behavioral measures indexing temporal perception. Accordingly, the present study was designed to address how stable individual differences in resting-state neural dynamics shape temporal performance, rather than within-task neural fluctuations during the temporal task. We agree that combining resting-state and task-related EEG would be a valuable direction for future work, but this lies beyond the scope of the current dataset, as EEG was not recorded during task performance. Furthermore, we agree with the Reviewers that some of the wording in the Discussion can be clarified to emphasize the trait-level, rather than trial-level, nature of the task and potential interpretations.

Additionally, we agree that the relationship between eyes-open (EO) and eyes-closed (EC) resting-state EEG, and their differential associations with behavior, warrants further discussion. In our data, EO resting-state activity emerged as a stronger predictor of behavioral performance than EC. Conceptually, resting-state EO and EC should not be considered interchangeable measures of the same underlying neural activity, but rather as related yet distinct brain states, with overlapping neural generators expressed under different state constraints. EC is typically associated with stronger posterior alpha activity and a more internally oriented mode, whereas EO reflects a more visually engaged and vigilant state, closer to the conditions under which perceptual judgments are formed. This may explain why, in our findings, brain–behavior associations are more evident in EO, consistent with the greater similarity between the EO condition and the task context. In this sense, EO may emphasize exteroceptive processing and visual readiness, whereas EC reflects a more internally oriented configuration. This difference in functional weighting could account for the stronger behavioral correlations observed in EO in the present study. The distinction between these resting states has been emphasized in previous EEG and neuroimaging work showing differences in power, topography, and large-scale network organization (e.g., Marx et al., 2004). Additionally, these state-related differences may reflect physiological changes related to sensory processing (El Boustani et al., 2009) and arousal (Lendner et al., 2020). Accordingly, the present dissociation may arise because EO provides a resting-state measure that is more proximal to the sensory and excitability conditions engaged during task performance (for similar findings, see also Deodato and Melcher, 2024). However, we agree with the reviewers that further clarification of these state-related differences is warranted. In the revised manuscript, we will (i) expand the Discussion to more clearly articulate the conceptual distinction between EO and EC and their expected links to perceptual and confidence measures, (ii) systematically describe EO–EC differences across all EEG measures analyzed, and (iii) quantify the relationship between EO and EC indices to directly assess the extent to which they share trait-like variance across individuals.

In the revised manuscript, we will clarify these points by adjusting the text, strengthening the conceptual framing, and expanding the Discussion, including a more detailed outline of future research directions.

(2) Functional interpretation of psychometric measures

The Reviewers raised an important point regarding the interpretation of the psychometric parameters investigated in our study. In particular, we agree that the slope of a binary psychometric function does not provide a direct measure of sensory temporal resolution or perceptual sensitivity, and that our original wording may have overstated this interpretation. Rather, the slope reflects the steepness of the transition between response categories and indexes overall behavioural variability, which can arise from multiple sources, including variability in sensory encoding, decision criteria, and occasional response errors (e.g., Wichmann and Hill 2001; Prins 2012).

We therefore agree that interpreting steeper slopes as necessarily reflecting “temporal precision” may be overly specific, and that there are other possible interpretations. In the revised manuscript, we will adopt more cautious terminology and describe the slope more generally as indexing behavioral variability in the transition between perceptual reports, which may reflect a combination of sensory and decisional factors. Importantly, our results demonstrate robust relationships between neural measures and the consistency or sharpness of perceptual categorization, rather than uniquely isolating sensory temporal resolution. While, in standard psychophysical frameworks, the slope is related to internal variability in the sensory representation, this relationship depends on model assumptions and does not uniquely isolate sensory precision (e.g., Prins, 2016). Following the reviewers’ suggestion, we will also refine our psychometric modeling by incorporating a lapse parameter. We agree with the Reviewer that accounting for occasional stimulus-independent errors (e.g., lapses) can improve parameter estimation and prevent biases in slope and threshold estimates when lapse rates are implicitly fixed to zero (Wichmann & Hill, 2001). In the revised manuscript, we will therefore (i) clarify the terminology used to describe psychometric parameters and (ii) report additional analyses including lapse rates.

In addition, we agree that complementary modeling approaches could help disentangle perceptual and decisional contributions to the observed effects by providing access to latent parameters of perceptual decision-making. For example, within a signal detection framework, one could test whether EEG measures relate to perceptual sensitivity versus decision criterion, while sequential sampling models such as the diffusion model (e.g., Ratcliff and McKoon, 2008) could assess whether neural measures are associated with parameters such as drift rate, decision boundary, starting bias, or trial-to-trial variability. However, several characteristics of the present paradigm limit the direct applicability of these approaches. First, the task relies on a continuous manipulation of sensory evidence across stimulus durations (ISIs), and behavioral responses are summarized through psychometric functions rather than modeled at the single-trial level. As a result, the current framework does not provide direct access to trial-by-trial latent decision variables required by these models. Second, reaction times were not collected, which constrains the application of sequential sampling models that rely on joint modeling of accuracy and response times. Finally, while the task involves categorical judgments (integration vs. segregation), it does not include explicit signal-absent or catch trials, which can help constrain sensitivity and criterion estimates within classical signal detection formulations. Despite these limitations, we agree that these approaches could still provide useful insights. In the revised manuscript, we will explore whether alternative modeling approaches (e.g., signal detection-based metrics or Bayesian psychometric modeling) can help further characterize the contributions of perceptual sensitivity, decision criterion, and response variability to our behavioral measures. While these analyses will necessarily remain exploratory given the structure of the current dataset, they may provide initial insights into whether the observed effects reflect perceptual or decisional dynamics. A more definitive dissociation, however, is beyond the scope of the present study and will be an important direction for future work.

(3) Control analyses and robustness of EEG–behavior relationships

The Reviewers raised interesting points regarding the interpretation of our control analyses and the potential influence of stimulus structure on the observed EEG–behavior relationships. We agree that these aspects require clarification and additional analyses to strengthen the robustness of our findings.

First, regarding the control analyses across frequency bands, we acknowledge that while our main analyses appropriately dissociate oscillatory and aperiodic components using spectral parameterization, the control analyses were based on conventional band-power measures. As correctly noted by the reviewers, band-limited power estimates can be influenced by the aperiodic background, which complicates the interpretation of null effects in the other frequency bands. In the revised manuscript, we will address this issue by extending our spectral parameterization approach to these control analyses. Specifically, we will recompute band-specific measures after removing the aperiodic component, allowing a clearer comparison across frequency bands and a more robust assessment of the specificity of alpha-related effects. Preliminary analyses suggest that these updated results are likely to be consistent with our initial findings, thereby reinforcing the robustness of the reported effects.

Another important point raised by the reviewers concerns the temporal structure of the stimulus stream. We agree that the continuous alternation of Gabor stimuli at varying durations introduces quasi-periodic stimulation rates that may induce entrainment of neural oscillations. Notably, some inter-stimulus intervals correspond to frequencies within the alpha range, which raises the possibility that the observed relationship between resting alpha frequency and integration thresholds may not solely reflect intrinsic sampling speed, but could also be influenced by the degree of alignment between an individual’s alpha rhythm and the temporal structure of the stimulus. As highlighted in prior work (e.g., Gulbinaite et al., 2017; Keitel et al., 2019; Gallina et al., 2023; Duecker et al., 2024), rhythmic stimulation in the alpha range can interact with intrinsic alpha oscillations and modulate both neural and perceptual processing. Although our study does not include EEG recordings during task performance and therefore cannot directly assess stimulus-locked responses or neural entrainment, we agree that this factor should be explicitly considered in the interpretation of our findings. To address this point, in the revised manuscript we will perform additional control analyses to assess the robustness of the observed relationships while accounting for potential rhythmic stimulation confounds. Specifically, we will explore whether the strength of behavioral effects and their relationship with EEG measures depends on the alignment between each participant’s individual alpha frequency and the effective stimulation rate induced by the stimulus presentation. In addition, we will test whether the association between resting-state alpha frequency and behavioral measures is disproportionately driven by stimulus durations corresponding to alpha-range temporal frequencies. These analyses will help determine whether the observed effects primarily reflect intrinsic sampling properties or are modulated by resonance-like interactions between endogenous rhythms and stimulus timing. We will also address all additional recommendations raised by the reviewers in the revised manuscript.

References

Demuru, M., & Fraschini, M. (2020). EEG fingerprinting: Subject-specific signature based on the aperiodic component of power spectrum. Computers in Biology and Medicine, 120, 103748.

Deodato, M., & Melcher, D. (2024). Correlations between visual temporal resolution and individual alpha peak frequency: Evidence that internal and measurement noise drive null findings. Journal of Cognitive Neuroscience, 36(4), 590-601.

Duecker, K., Doelling, K. B., Breska, A., Coffey, E. B., Sivarao, D. V., & Zoefel, B. (2024). Challenges and Approaches in the Study of Neural Entrainment. Journal of Neuroscience, 44(40).

El Boustani, S., Marre, O., Béhuret, S., Baudot, P., Yger, P., Bal, T., ... & Frégnac, Y. (2009). Network-state modulation of power-law frequency-scaling in visual cortical neurons. PLoS computational biology, 5(9), e1000519.

Euler, M. J., Vehar, J. V., Guevara, J. E., Geiger, A. R., Deboeck, P. R., & Lohse, K. R. (2024). Associations between the resting EEG aperiodic slope and broad domains of cognitive ability. Psychophysiology, 61(6), e14543.

Gallina, J., Marsicano, G., Romei, V., & Bertini, C. (2023). Electrophysiological and Behavioral Effects of Alpha-Band Sensory Entrainment: Neural Mechanisms and Clinical Applications. Biomedicines, 11(5), 1399.

Grandy, T. H., Werkle‐Bergner, M., Chicherio, C., Schmiedek, F., Lövdén, M., & Lindenberger, U. (2013). Peak individual alpha frequency qualifies as a stable neurophysiological trait marker in healthy younger and older adults. Psychophysiology, 50(6), 570-582.

Gray, M. J., & Emmanouil, T. A. (2020). Individual alpha frequency increases during a task but is unchanged by alpha‐band flicker. Psychophysiology, 57(2), e13480.

Gulbinaite, R., Van Viegen, T., Wieling, M., Cohen, M. X., & VanRullen, R. (2017). Individual alpha peak frequency predicts 10 Hz flicker effects on selective attention. Journal of Neuroscience, 37(42), 10173-10184.

Keitel, C., Keitel, A., Benwell, C. S., Daube, C., Thut, G., & Gross, J. (2019). Stimulus-driven brain rhythms within the alpha band: The attentional-modulation conundrum. Journal of Neuroscience, 39(16), 3119-3129.

Lendner, J. D., Helfrich, R. F., Mander, B. A., Romundstad, L., Lin, J. J., Walker, M. P., ... & Knight, R. T. (2020). An electrophysiological marker of arousal level in humans. elife, 9, e55092.

Marx, E., Deutschländer, A., Stephan, T., Dieterich, M., Wiesmann, M., & Brandt, T. (2004). Eyes open and eyes closed as rest conditions: impact on brain activation patterns. Neuroimage, 21(4), 1818-1824.

Pathania, A., Euler, M. J., Clark, M., Cowan, R. L., Duff, K., & Lohse, K. R. (2022). Resting EEG spectral slopes are associated with age-related differences in information processing speed. Biological Psychology, 168, 108261.

Prins, N. (2012). The psychometric function: The lapse rate revisited. Journal of Vision, 12(6), 25-25.

Prins, N. (2016). Psychophysics: a practical introduction. Academic Press.

Ratcliff, R., & McKoon, G. (2008). The diffusion decision model: theory and data for two-choice decision tasks. Neural computation, 20(4), 873-922.

Wichmann, F. A., & Hill, N. J. (2001). The psychometric function: I. Fitting, sampling, and goodness of fit. Perception & psychophysics, 63(8), 1293-1313.

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eLife Assessment

This important study presents convincing evidence that uncovers a novel signaling axis impacting the post-mating response in females of the brown planthopper. The findings open several avenues for testing the molecular and neurobiological mechanisms of mating behavior in insects, and in the revised version the authors provide further evidence supporting their conclusions.

Reviewer #2 (Public review):

Summary:

The work presented by Zhang and coauthors in this manuscript presents the study of the neuropeptide corazonin in modulating the post-mating response of the brown planthopper, with further validation in Drosophila melanogaster. To obtain their results, the authors used several different techniques that orthogonally demonstrate the involvement of corazonin signalling in regulating the female post-mating response in these species.

They first injected synthetic corazonin peptide into female brown planthoppers, showing altered mating receptivity in virgin females and a higher number of laid eggs after mating. The role of corazonin in controlling these post-mating traits has been further validated by knocking down the expression of the corazonin gene by RNA interference and through CRISPR-Cas9 mutagenesis of the gene. Further proof of the importance of corazonin signaling in regulating the female post-mating response has been achieved by knocking down the expression or mutagenizing the gene coding for the corazonin receptor.

Similar results have been obtained in the fruit fly Drosophila melanogaster, suggesting that corazonin signaling is involved in controlling the female post-mating response in multiple insect species.

The study of the signalling pathways controlling the female post-mating response in insects other than Drosophila is scarce, and this limits the ability of biologists to draw conclusions about the evolution of the post-mating response in female insects. This is particularly relevant in the context of understanding how sexual conflict might work at the molecular and genetic levels, and how, ultimately, speciation might occur at this level. Furthermore, the study of the post-mating response could have practical implications, as it can lead to the development of control techniques, such as sterilization agents.

The study, therefore, expands the knowledge of one of the signalling pathways that control the female post-mating response, the corazonin neuropeptide. This pathway is involved in controlling the post-mating response in both Nilaparvata lugens (the brown planthopper) and Drosophila melanogaster, suggesting its involvement in multiple insect species.

The study uses multiple molecular approaches to convincingly demonstrate that corazonin controls the female post-mating response. The data supporting the main claim of the manuscript are solid and convincing.

Author Response:

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

eLife Assessment

This important study presents convincing evidence that uncovers a novel signaling axis impacting the post-mating response in females of the brown planthopper. The findings open several avenues for testing the molecular and neurobiological mechanisms of mating behavior in insects, although broad concerns remain about the relevance of some claims.

Thank you very much for your letter and the insightful, valuable comments from the reviewers on our manuscript. These suggestions have been instrumental in strengthening the quality and clarity of our work. We have carefully addressed each concern, performed additional experiments, revised the relevant sections thoroughly, and made extensive refinements to the Discussion to clarify future research directions. Below is our detailed point-by-point response.

Public Reviews:

Reviewer #1 (Public review):

In this work, Zhang et al, through a series of well-designed experiments, present a comprehensive study exploring the roles of the neuropeptide Corazonin (CRZ) and its receptor in controlling the female post-mating response (PMR) in the brown planthopper (BPH) Nilaparvata lugen and Drosophila melanogaster. Through a series of behavioural assays, micro-injections, gene knockdowns, Crispr/Cas gene editing, and immunostaining, the authors show that both CRZ and CrzR play a vital role in the female post-mating response, with impaired expression of either leading to quicker female remating and reduced ovulation in BPH. Notably, the authors find that this signaling is entirely endogenous in BPH females, with immunostaining of male accessory glands (MAGs) showing no evidence of CRZ expression. Further, the authors demonstrate that while CRZ is not expressed in the MAGs, BPH males with Crz knocked out show transcriptional dysregulation of several seminal fluid proteins and functionally link this dysregulation to an impaired PMR in BPH. In relation, the authors also find that in CrzR mutants, the injection of neither MAG extracts nor maccessin peptide triggered the PMR in BPH females. Finally, the authors extend this study to D. melanogaster, albeit on a more limited scale, and show that CRZ plays a vital role in maintaining PMR in D. melanogaster females with impaired CRZ signaling, once again leading to quicker female remating and reduced ovulation. The authors must be commended for their expansive set of complementary experiments. The manuscript is also generally well written. Given the seemingly conserved nature of CRZ, this work is a significant addition to the literature, opening several avenues for testing the molecular and neurobiological mechanisms in which CRZ triggers the PMR.

However, there are some broad concerns/comments I had with this manuscript. The authors provide clear evidence that CRZ signaling plays a major role in the PMR of D. melanogaster, however, they provide no evidence that CRZ signaling is endogenous, as they did not check for expression in the MAGs of D. melanogaster males. Additionally, while the authors show that manipulating Crz in males leads to dysregulated seminal fluid expression and impaired PMR in BPH, the authors also find that CRZ injection in males in and of itself impairs PMR in BPH. The authors do not really address what this seemingly contradictory result could mean. While a lot of the figures have replicate numbers, the authors do not factor in replicate as an effect into their models, which they ideally should do. Finally, while the discussion is generally well-written, it lacks a broader conclusion about the wider implications of this study and what future work building on this could look like.

Thank you very much for your insightful and valuable comments on our manuscript. We have carefully addressed each of your concerns, revised the relevant sections thoroughly, and conducted additional experiments to further strengthen our conclusions. To better focus on the core finding of this study, the critical role of Crz/CrzR signaling in regulating the post-mating response (PMR) of female brown planthoppers (BPH), and to eliminate potential confusion associated with the male-related data, we have removed the experiments investigating CRZ function in males from the current version of the manuscript. These observations on male CRZ signaling will be explored in greater depth and presented as a standalone study in a separate manuscript in the future.

Reviewer #2 (Public review):

Summary:

The work presented by Zhang and coauthors in this manuscript presents the study of the neuropeptide corazonin in modulating the post-mating response of the brown planthopper, with further validation in Drosophila melanogaster. To obtain their results, the authors used several different techniques that orthogonally demonstrate the involvement of corazonin signalling in regulating the female post-mating response in these species.

They first injected synthetic corazonin peptide into female brown planthoppers, showing altered mating receptivity in virgin females and a higher number of eggs laid after mating. The role of corazonin in controlling these post-mating traits has been further validated by knocking down the expression of the corazonin gene by RNA interference and through CRISPR-Cas9 mutagenesis of the gene. Further proof of the importance of corazonin signalling in regulating the female post-mating response has been achieved by knocking down the expression or mutagenizing the gene coding for the corazonin receptor.

Similar results have been obtained in the fruit fly Drosophila melanogaster, suggesting that corazonin signalling is involved in controlling the female post-mating response in multiple insect species.

Notably, the authors also show that corazonin controls gene expression in the male accessory glands and that disruption of this pathway in males compromises their ability to elicit normal post-mating responses in their mates.

Strengths:

The study of the signalling pathways controlling the female post-mating response in insects other than Drosophila is scarce, and this limits the ability of biologists to draw conclusions about the evolution of the post-mating response in female insects. This is particularly relevant in the context of understanding how sexual conflict might work at the molecular and genetic levels, and how, ultimately, speciation might occur at this level. Furthermore, the study of the post-mating response could have practical implications, as it can lead to the development of control techniques, such as sterilization agents.

The study, therefore, expands the knowledge of one of the signalling pathways that control the female post-mating response, the corazonin neuropeptide. This pathway is involved in controlling the post-mating response in both Nilaparvata lugens (the brown planthopper) and Drosophila melanogaster, suggesting its involvement in multiple insect species.

The study uses multiple molecular approaches to convincingly demonstrate that corazonin controls the female post-mating response.

Thank you very much for your valuable and insightful comments on our manuscript. We highly appreciate your recognition of the study’s value, including its focus on non-model insects, the evolutionary implications of corazonin signaling, and the rigorous use of multiple molecular techniques. We have carefully addressed your suggestions and revised the manuscript accordingly to enhance its clarity, accuracy, and depth. Below is our detailed response to your comments.

Weaknesses:

The data supporting the main claims of the manuscript are solid and convincing. The statistical analysis of some of the data might be improved, particularly by tailoring the analysis to the type of data that has been collected.

Thank you for your valuable suggestion regarding statistical analysis. We fully agree that tailoring statistical methods to the specific type of data enhances the rigor and reliability of our findings.

In response, we have comprehensively re-evaluated and revised the statistical analyses for all datasets in the manuscript:

(1) For proportion-based data (e.g., female mating receptivity, re-mating rate), we replaced inappropriate tests (e.g., ANOVA) with chi-square tests for contingency tables, which are more suitable for comparing categorical variables.

(2) For time-series data (e.g., receptivity at different time points post-injection), we adopted generalized linear models (GLM) with logit links followed by pairwise contrasts to address concerns of multiple testing, instead of hour-by-hour Mann-Whitney tests.

(3) For continuous data (e.g., number of eggs laid, gene expression levels), we retained Student’s t-tests or one-way ANOVA after verifying normality, and used non-parametric tests (Mann-Whitney, Kruskal-Wallis) for non-normally distributed data.

All revisions have been clearly described in the figure legends and Methods section, ensuring transparency and reproducibility. We believe these adjustments significantly improve the statistical robustness of our conclusions.

In the case of the corazonin effect in females, all the data are coherent; in the case of CRISPR-Cas9-induced mutagenesis, the analysis of the behavioural trait in heterozygotes might have helped in understanding the haplosufficiency of the gene and would have further proved the authors' point.

Thank you for this insightful suggestion. We fully agree that analyzing the behavioral traits of heterozygous mutants is crucial for understanding the haplosufficiency of the Crz and CrzR genes, and we regret overlooking this aspect in the initial submission.

To address this gap, we have conducted additional behavioral assays using heterozygous Crz (+/ΔCrz) and CrzR (+/CrzR^M) mutant females.

(1) For re-mating receptivity: We found no significant differences in either re-mating rate or egg-laying output between +/ΔCrz females and wild-type females. By contrast, +/CrzR^M females exhibited re-mating and oviposition phenotypes comparable to those of homozygous CrzR mutants, with no significant differences detected between these two genotypes.

(2) These results indicate that the Crz loss-of-function phenotype is recessive, and that a single functional copy of Crz is sufficient to sustain a normal post-mating response (PMR), but the CrzR loss-of-function phenotype is dominant, and that a single functional copy of CrzR is insufficient to maintain a normal post-mating response.

This supports our core conclusion that CRZ signaling is critical for mediating the female PMR, as even partial reduction of gene dosage impairs the response.

The heterozygote data have been integrated into the revised manuscript, including updated figures (e.g., Figure 1J-K for Crz heterozygotes and Figure 3I-J for CrzR heterozygotes) and corresponding legends. We believe this addition strengthens the rigor of our genetic evidence and provides valuable insights into the gene dosage requirements for CRZ-mediated PMR regulation.

Less consistency was achieved in males (Figure 5): the authors show that injection of CRZ and RNAi of crz, or mutant crz, has the same effect on male fitness. However, the CRZ injection should activate the pathway, and crz RNAi and mutant crz should inhibit the pathway, yet they have the same effect. A comment about this discrepancy would have improved the clarity of the manuscript, pointing to new points that need to be clarified and opening new scientific discussion.

Thank you for highlighting this important discrepancy in the male-related CRZ signaling data. We fully acknowledge the inconsistency: CRZ injection (which was intended to activate the pathway) and Crz RNAi/mutagenesis (which was intended to inhibit the pathway) yielded similar effects on male fitness, and we regret not addressing this ambiguity in the initial submission.

To resolve this confusion and refocus the current manuscript on its core objective—elucidating the role of endogenous CRZ/CrzR signaling in female post-mating response (PMR), we have removed all experiments, analyses, and discussions related to male CRZ function. This decision ensures that the manuscript maintains a clear, cohesive narrative centered on female reproductive physiology, as recommended by both reviewers and the editorial team.

Regarding the observed discrepancy in males, we recognize its scientific significance and plan to investigate it thoroughly in a standalone follow-up study.

Recommendations for the authors:

Reviewing Editor Comments:

The manuscript would be significantly strengthened by an explanation of the seemingly contradictory results obtained in males, where both CRZ injections and Crz silencing afford the same results. Additionally, Crz expression data in the MAGs of D. melanogaster males is necessary to support your conclusions of endogenous signaling in this species. Besides correcting several imprecisions and inconsistencies in the text and figures, to improve quality and accuracy, the abstract should be restructured and the discussion modified as recommended by reviewers.

Thank you for your comprehensive letter and valuable guidance. We have carefully addressed all the points raised by the editorial team and reviewers, and the revised manuscript now incorporates substantial improvements to clarity, accuracy, and scientific rigor. Below is our detailed response to your specific requests:

Contradictory Male-Related Results

We fully acknowledge the importance of addressing the contradictory findings in male CRZ signaling, where both CRZ injection and Crz silencing/mutagenesis yielded similar effects on male fitness. To resolve this ambiguity and maintain the manuscript’s focus on its core objective, elucidating endogenous CRZ/CrzR signaling in the female post-mating response (PMR), we have removed all male-related experiments, analyses, and discussions from the revised manuscript. This decision ensures that the current work remains cohesive and centered on female reproductive physiology, as recommended by the reviewers.

We recognize the scientific significance of the male-specific discrepancy and plan to investigate it in a standalone follow-up study in the near future.

Crz expression data in D. melanogaster Male Accessory Glands (MAGs)

To support our conclusion of endogenous CRZ signaling in D. melanogaster females, we have supplemented the manuscript with additional experiments verifying the absence of CRZ in male MAGs:

(1) RT-PCR Analysis: We detected no Crz mRNA in dissected male MAGs, whereas Crz expression was confirmed in the male head (positive control).

(2) Immunohistochemistry and GAL4 system: Using the GAL4–UAS system (Crz-Gal4/UAS-mCD8-GFP) to label CRZ-producing neurons, combined with anti-CRZ antibody staining, we observed no CRZ-specific signal in male MAGs.

These results demonstrate that D. melanogaster male MAGs neither synthesize nor contain CRZ peptide, confirming that CRZ acts as an endogenous female signaling factor (rather than a male-transferred seminal fluid component) in this species. The new data are included in Figure 5H-I and described in the Results and Methods sections.

Correction of Imprecisions and Inconsistencies

We have systematically revised the manuscript to address text and figure inaccuracies:

Text Revisions: Corrected typos (e.g., Line 854), standardized species names (replacing “Drosophila” with “D. melanogaster” throughout), removed redundant or inappropriate sentences, and refined terminology (e.g., replacing “expression” with “localization” for protein detection).

Figure Corrections: Fixed inconsistent Y-axis labels and numerical ranges (e.g., aligning percentages/probabilities with appropriate scales), resolved color scheme confusion, standardized oviposition-related labels to “Per female egg numbers within 3 days,” and added details on sample sizes and replicates to all figure legends.

Statistical Improvements: Re-evaluated statistical analyses for proportion-based datasets (applying chi-square tests for contingency tables) and time-series data (using generalized linear models to address multiple testing), with revised methods clearly described in the text and figure legends.

Abstract Restructuring and Discussion Modification

Abstract: We have restructured the abstract to group results thematically (rather than sequentially) for improved readability. The revised abstract emphasizes the core findings: CRZ/CrzR signaling is critical for female PMR in both N. lugens and D. melanogaster, acts endogenously in females, and is required for male seminal fluid factors to induce PMR. Male-related content has been removed since experimental data are deleted from the rest of the paper.

Discussion: We have modified the discussion to include the evolutionary conservation of CRZ-mediated female PMR, the molecular and neurobiological implications of CRZ/CrzR signaling, and future research directions (e.g., dissecting downstream pathways in the female reproductive tract and brain). We have also reduced tangential content and clarified how our findings advance understanding of female endogenous signaling in PMR regulation. A new section was added at the end, which discusses outstanding questions related to CRZ and the PMR in both insect species.

To both the above-mentioned sections and the Introduction we also added new text to emphasize that CRZ is a paralog of the vertebrate peptide gonadotropin-releasing hormone (GnRH), a hormone known to regulate reproduction in vertebrates (including humans), thus suggesting conservation of an ancient role in reproduction.

All revisions in the manuscript are highlighted in red for easy reference. We believe these changes significantly strengthen the study’s focus, clarity, and scientific impact. Thank you again for your time and consideration.

Reviewer #1 (Recommendations for the authors):

(1) The abstract could benefit from some restructuring. Right now, it reads like a sequential reporting of the results, but clumping together results thematically would make it easier to read, in my opinion. Also, see above re: my concerns about no evidence for the signal being endogenous in D. melanogaster.

Thank you for your constructive suggestions regarding the abstract and the evidence for endogenous CRZ signaling in D. melanogaster. We fully agree with your feedback and have addressed both points thoroughly in the revised manuscript:

(1) Abstract Restructuring

We have restructured the abstract to group results thematically, rather than sequentially, to enhance readability and highlight the core findings. The revised abstract now organizes key information into three cohesive sections:

The context and significance of female post-mating response (PMR) regulation, emphasizing the gap in understanding endogenous female signaling pathways.

The core findings across both study species (Nilaparvata lugens and D. melanogaster), including the critical role of CRZ/CrzR signaling in suppressing re-mating and promoting oviposition, and its requirement for male seminal fluid factors to induce a PMR.

The conclusion regarding the evolutionary conservation of endogenous CRZ signaling in female PMR, reinforcing the study’s broader implications.

We also added new text to emphasize that CRZ is a paralog of the vertebrate peptide gonadotropin-releasing hormone (GnRH), a hormone known to regulate reproduction in vertebrates (including humans), thus suggesting conservation of an ancient role in reproduction.

This thematic structure eliminates the linear “result-by-result” narrative, making the abstract more concise and impactful while clearly communicating the study’s key contributions.

(2) Evidence for Endogenous CRZ Signaling in female D. melanogaster

To address your concern about the lack of evidence for endogenous signaling in female D. melanogaster, we have supplemented the manuscript with two sets of critical experiments confirming that CRZ is not derived from male accessory glands (MAGs) but acts endogenously in females:

RT-PCR Analysis: We performed RT-PCR on dissected male MAGs, male heads (positive control), and female tissues. Results showed no detectable Crz mRNA in MAGs, confirming that males do not synthesize CRZ in this tissue.

Immunohistochemical and Genetic Labeling: Using the GAL4–UAS system (Crz-Gal4/UAS-mCD8-GFP) to label Crz-expressing neurons, combined with anti-CRZ antibody labeling, we observed no crz/CRZ signal in male MAGs. This confirms that MAGs neither produce nor sequester mature CRZ peptide.

These findings demonstrate that CRZ signaling in D. melanogaster females is endogenous, as the peptide cannot be transferred from males during copulation. The new data are presented in Figure 5H-I and described in the Results section, with corresponding methods detailed in the Methods section.

The revised abstract integrates this new evidence to explicitly state the endogenous nature of CRZ signaling in both BPH and D. melanogaster females, aligning with the thematic structure and addressing your concerns comprehensively. We believe these changes significantly improve the clarity and rigor of the abstract and the manuscript overall.

(2) The authors use Drosophila as a broad placeholder throughout the manuscript, while they are specifically referring to D. melanogaster in several places. I would go through the manuscript and switch with the appropriate Drosophila species/species'.

Thank you for pointing out this important detail regarding species-specific terminology. We fully agree with your suggestion to ensure accuracy and consistency in referencing the Drosophila species studied.

We have systematically reviewed the entire manuscript, including the abstract, introduction, results, discussion, methods, and figure legends, and revised all instances where the general term “Drosophila” was used. All references now explicitly specify “D. melanogaster” to accurately reflect the species utilized in our experiments.

(3) For the figures, I think the number of replicates is a distracting addition to the plot. This is still useful information, but could instead be added in as a line/table, in my opinion.

Thank you very much for your suggestion. We have added the information on the number of replicates and sample sizes to the corresponding figure legends, which we hope improves clarity and readability.

(4) There are typos in the y-axis label of all of the oviposition figures. A better re-wording would be "Per female egg numbers within 3 days".

Thank you very much for your suggestion. Following your recommendation, we have now standardized the Y-axis label for all oviposition-related figures to “Number of eggs per female within 3 days.”

(5) In Figure 1B and Figure 1 - Supplement 3a, since the comparisons are solely between control vs treatment, I would not join means across treatments that I am not comparing.

To address this, we have revised Figure 1B and Figure 1—Supplement 3a by removing the connecting lines between group means. The updated figures now display independent mean ± SEM values for each dose (Figure 1B) and time point (Figure 1—Supplement 3a), with significance markers only applied to the control vs. treatment comparisons we actually tested. This revision eliminates any implied relationships between non-comparative groups and ensures the data visualization aligns with our statistical approach. We appreciate the reviewer’s suggestion, which has improved the clarity of the data presentation.

(6) The authors mention courtship rate in lines 511, but from a look at the methods, this is not the courtship rate! This is a measure of the number of males engaging in any form of courtship. Also, in Figure 5 Supplement 2A, it appears that under 1% of males are courting. This seems extremely low. Do the authors mean percentages? In that case, I would reformat from 0 to 100/relabel the y-axis.

Thank you for your observation and valuable feedback on this terminology and figure presentation issue. We fully acknowledge the inaccuracies and have addressed them comprehensively:

(1) Correction of "Courtship Rate" Terminology

We agree that the term “courtship rate” in Line 511 was incorrect, as our measurement reflects the proportion of males engaging in any form of courtship (not a rate per unit time). However, since we have removed all male-related data (including this section and associated figures) from the revised manuscript to focus on the core finding of female post-mating response (PMR), this terminology error has been eliminated entirely.

(2) Revision of Figure 5 Supplement 2A

Consistent with the removal of all male-related experiments, Figure 5 and its supplementary materials (including Supplement 2A) have been excluded from the revised manuscript. This ensures the current work remains cohesive and centered on female PMR, while also resolving the Y-axis labeling ambiguity you identified.

We appreciate your careful attention to these details, which helps enhance the accuracy and clarity.

(7) It appears Figure 5A, 5D, and 5G are mislabeled? Aren't all rematings with wild-type males?

Thank you for identifying this labeling inconsistency. You are absolutely correct, all re-mating assays in the original figures involved wild-type males, and the mislabeling was an oversight.

However, we have removed Figure 5 (and its associated subpanels A, D, G) entirely from the revised manuscript, as part of our decision to exclude all male-related data.

(8) I am not sure I understand why a 30-minute post-injection threshold was chosen and what this table means. Could the authors elaborate on the methodology here on how they quantified premature ejaculation?

Thank you for your question regarding the 30-minute post-injection observation window and the methodology for quantifying premature ejaculation.

While we have removed all male-related data (including the corresponding table and premature ejaculation analyses) from the revised manuscript to focus on our core finding, this is no longer included in the manuscript.

(9) Line 29 - "distensible" seems an odd choice of word here.

We have revised Line 29 and removed “distensible”. “Peptide injection and knockdown of CRZ expression by RNAi or CRISPR/Cas9-mediated mutagenesis demonstrate that CRZ signaling suppresses mating receptivity”.

(10) Line 57 - delete "a" from "a post-mating response" and "A PMR" because the authors are referring to a very specific suite of post-mating behaviours.

We have revised Line 57 (and other relevant instances throughout the manuscript) to delete the article "a" from these phrases.

(11) Line 352, delete a from "and in a significantly".

We have revised Line 356 to remove the extraneous "a", correcting the phrase to "and in significantly".

Reviewer #2 (Recommendations for the authors):

The work presented in this manuscript presents the study of the neuropeptide corazonin in modulating the post-mating response of the brown planthopper, with further validation in Drosophila melanogaster. To obtain their results, the authors used several different techniques, including dsRNA injection to induce RNA interference and CRISPR-CAS9-mediated site-specific mutagenesis. The experimental design is appropriate; the results are solid and support the conclusion of the manuscript. Overall, the merit of the manuscript is to present compelling evidence that the female post-mating response is mediated by corazonin, at least in the analysed species. There are multiple reports in multiple insect species, indeed, that male factors, particularly those secreted by male accessory glands, induce post-mating response in females, but the female pathways underlying this phenomenon are poorly understood.

There are points the authors can consider to improve the manuscript quality.

Thank you for your generous and insightful assessment of our manuscript. We deeply appreciate your recognition of the study’s strengths, including the appropriate experimental design, solid results, and meaningful contribution to understanding female endogenous pathways in post-mating response (PMR) regulation.

We have carefully incorporated all your constructive suggestions (e.g., statistical analysis revisions, figure label standardization, text refinements) to further strengthen the manuscript’s rigor and clarity. By focusing on corazonin (CRZ/corazonin receptor (CrzR) signaling in female brown planthoppers (Nilaparvata lugens) and validating these findings in Drosophila melanogaster, we aim to provide a conserved model for female endogenous PMR regulation across insect species.

Thank you again for your thoughtful and supportive feedback, which has been instrumental in refining our work. We believe the revised manuscript now more effectively communicates the significance of CRZ-mediated female signaling in bridging the gap between male-derived cues and PMR execution.

(1) Line 20: "optimal offspring". This is not a zoological parameter. One can use "optimal fitness".

We have revised Line 20 to replace "optimal offspring" with "optimal fitness" as recommended.

(2) Line 36-40: I think that the main message of the manuscript is the involvement of the corazonin pathway in controlling the female post-mating response. The involvement of corazonin in the male reproduction is also of note, but out of topic (in my opinion). The male corazonin is not transferred during mating from males to females, and the involvement of corazonin in controlling the gene expression in the MAGs is of note, but it is poorly related to the effect of corazonin in the female. I am not suggesting removing these data from the paper; they are important. But I do not find them that important to include them in the abstract, also because it confounds the reader at first. A similar statement can be made for the discussion (lines 728-745): making this the first piece of data commented on takes the stage, but this is not the main take-home message of the paper.

Thank you for this suggestion. We fully agree that including male-related CRZ data in the abstract and leading the discussion with these results distracted from the primary focus and risked confounding readers. In fact, we also removed the entire section on the role of CRZ in males. We have addressed this issue comprehensively in the revised manuscript as follows:

(1) Abstract Revision

We have completely removed all content related to male CRZ function from the revised abstract. The updated abstract now exclusively emphasizes the core findings:

The requirement of CRZ/CrzR signaling for mediating key female PMR traits (suppression of remating, promotion of oviposition) in both Nilaparvata lugens and Drosophila melanogaster;

Experimental evidence confirming that CRZ acts as an endogenous female signaling factor (not a male-transferred molecule);

The evolutionary conservation of CRZ-mediated female PMR regulation across the two insect species.

We also added a comment on the evolutionary conservation of CRZ and GnRH signaling in reproduction.

(2) Discussion Section Restructuring

We have restructured the Discussion to prioritize the core message of female PMR regulation:

Lead paragraph adjustment: Lines 728–745 (originally focusing on male CRZ and MAG gene expression) have been deleted.

Revised opening focus: The Discussion now only contain a synthesis of our key findings on female CRZ signaling, including its molecular mechanisms, cross-species conservation, and implications for understanding endogenous female pathways downstream of male seminal fluid cues.

We appreciate your suggestions for the narrative focus of the manuscript.

(3) Line 49: "Reproductive behavior is critical for population sustenance and survival of the species": I find this intro a little teleological evolutionary speaking, and I am not totally sure that this has ever been demonstrated as a concept. I would skip it, simply saying "Reproductive behavior in insects is influenced...".

Following your suggestion, we have revised Line 49 to streamline the introduction and avoid “teleological language”. The updated sentence now reads: "Reproductive behavior in insects is influenced by a complex interplay of neural, hormonal, and environmental factors."

(4) Line 58: "A PMR has been documented across diverse insect taxa, including Drosophila melanogaster, Anopheles gambiae, Aedes aegypti, and the brown planthopper (BPH), Nilaparvata lugens". There are many other insect species for which PMR has been shown: crickets, fruit flies, grasshoppers, etc. Therefore, I would say "for example" to underline that it is not a complete list. Being an incomplete list, I suggest that the authors pay attention to the cited literature: the literature cited in the case of Anopheles gambiae demonstrates the synthesis of hormones in the MAGs, but it has nothing to do with PMR; there is nothing cited for Aedes aegypti, even if the authors named the species.

Thank you for this constructive feedback on the framing of PMR studies across insect taxa and the accuracy of our cited literature. We fully agree with your suggestions and have addressed these issues comprehensively in the revised manuscript:

(1) Revision of the Sentence Structure

We have modified Line 58 to explicitly indicate that the listed species are examples rather than a complete inventory of insects with documented PMR. The revised sentence reads:

"The PMR has been documented across diverse insect taxa, for example, Drosophila melanogaster, Anopheles gambiae, Aedes aegypti, crickets (Gryllodes sigillatus), grasshoppers (Dichromorpha viridis), and the brown planthopper (BPH), Nilaparvata lugens"

(2) Correction of Literature Citations

We have thoroughly reviewed the citations associated with the listed species to ensure they directly support the role of PMR:

For Anopheles gambiae: We have replaced the previously cited study (focused on MAG hormone synthesis) with two relevant references that explicitly characterize PMR traits—including mating-induced oviposition stimulation and remating suppression—in this mosquito species.

For Aedes aegypti: We have added two newly published studies that document key PMR phenotypes (e.g., post-mating refractoriness and altered feeding behavior) and their underlying molecular mechanisms in this species.

For crickets (Gryllodes sigillatus): We added a newly published study that documents PMR phenotypes in Gryllodes sigillatus.

We have also verified that the citations for D. melanogaster and N. lugens remain directly relevant to PMR regulation, with no adjustments needed.

All revised citations are properly formatted and integrated into the text, with corresponding updates to the reference list.

(5) Line 111-132: I find this redundant: it is a long summary of the methods and the results. I do not think it is needed here, but I think the authors should point to the main message of their data.

Thank you for pointing out the redundancy of Lines 111–132. We fully agree that this section, disrupted the flow of the introduction of our study.

To address this, we have completely removed Lines 111–132 from the revised manuscript. In place of this redundant content, we have added a concise, focused paragraph that emphasizes the central hypothesis and key objective of our work: specifically, to identify the endogenous female signaling pathways that mediate the post-mating response (PMR) downstream of male-derived cues, and to validate the conserved role of corazonin (CRZ) signaling in this process across Nilaparvata lugens and Drosophila melanogaster.

(6) Line 156: This sentence is not needed here.

We have deleted the sentence in Line 156 from the revised manuscript.

(7) Figure 1E, J supplementary 3A: The label of the Y axis is the percentage of the mating females (expected 0-100%), but the numbers show the fraction (0-1). On the contrary, in Figure 1 Supplement 4, the label says "probability of survival" and the probability goes from 0 to 1, while the number of the axis goes from 0 to 100 (percentage).

Thank you very much for pointing out these inconsistencies. We have carefully reviewed all Y-axis labels and corresponding numerical ranges throughout the manuscript and corrected the mismatched axes.

(8) Figure1B, C, F, K supp 2, 3A: I found this use of colours confounding. Why did the authors use the light blue for sCRZ, but the mean and SE are shown in pink, which is the colour for CRZ? Furthermore, it is not reported anywhere how many individuals have been used per replicate. There is the total number of insects, the number of replicates, but there is no indication about the minimum number of insects per replicate in this and many other subsequent experiments.

Thank you for identifying these critical inconsistencies in figure color coding and missing details on sample allocation per replicate, and we greatly appreciate your meticulous review of our data presentation.

We have addressed these issues in the revised manuscript as follows:

(1) Standardization of Color Coding

We apologize for the confusing color mismatch between group labels and data points in Figure 1B, C, F, K, and Supplements 2 and 3A. We have unified the color scheme across some figures to ensure consistency:

The sCRZ (control) group is now consistently represented by light blue for both labels and mean ± SE data points.

The CRZ (treatment) group is now consistently represented by pink for both labels and mean ± SE data points.

For Figures 1C, F, K and Supplementary Figure 2, we were concerned that the mean and s.e.m. bars might be visually obscured by the data points. To improve their visibility, we therefore used the opposite color to display the mean and s.e.m.

All figure legends have been cross-checked and updated to reflect this standardized color coding.

(2) Addition of Sample Size per Replicate

We acknowledge that the lack of information on the minimum number of insects per replicate was a key gap in our experimental reporting. We have supplemented this critical detail in this way:

Figure Legends: For Figure 1B, C, F, K, and Supplements 2 and 3A (as well as all subsequent experiments), we have added explicit statements specifying the minimum number of insects per replicate, alongside the total sample size and number of replicates (e.g., “n = 3 replicates, with a minimum of 10 females per replicate; total N = 35 females”). All revised figures and their corresponding legends have been integrated into the updated manuscript, and we have cross-checked all other figures to avoid similar issues.

(9) Figure 1C, F, K, Supplementary Figure 3B: Y axis labels - "Eggs numbers of per female...". I suggest changing it to "Number of eggs per female...".

We have revised the Y-axis labels for Figure 1C, F, K and Supplementary Figure 3B to Number of eggs per female...” as recommended. Additionally, we cross-checked all other oviposition-related figures in the manuscript to ensure uniform use of this standardized label, eliminating any inconsistent phrasing across the dataset.

(10) Legend Figure 1B: Mann Whitney test. How did the authors perform the test? Hour by hour? I am not sure this is the best way to analyse the data, because it is a case of multiple testing. Probably a linear model or a glm might be a better fit.

Thank you very much for pointing out this issue. In Figure 1B, each concentration group was analyzed using data from independent individuals, and therefore the comparisons do not involve repeated measures across time; for this reason, we consider the Mann–Whitney test appropriate for this dataset. For Figure 1—Supplement 3A, however, our original analysis compared treatment and control groups hour by hour, which indeed raises concerns regarding multiple testing. Following your suggestion, we have removed the potentially misleading connecting lines and reanalyzed the dataset using a generalized linear model (GLM). The updated figure and revised legend have been included in the revised manuscript.

(11) Legend Figure 1E: ANOVA test. These are proportions, not continuous variables of the samples. Tests for proportions might be a better fit (chi-square, etc.).

To address this issue, we have re-analyzed the proportional data in Figure 1E using Pearson’s chi-square test of independence, which directly evaluates the association between treatment group (sCRZ vs. CRZ) and the binary mating status (mated vs. unmated) of females. This test is statistically robust for proportional data and avoids the assumptions of normality and homogeneity of variances required for ANOVA.

(12) Knockout experiments: I agree with the authors that the data are strong enough to sustain the conclusions. However, is the corazonin knockout haplosufficient or is it recessive? What is the behaviour of the heterozygotes?

Thank you for this insightful question regarding the genetic basis of the corazonin (CRZ) knockout phenotype.

To address your query, we have supplemented experiments with additional phenotypic analyses of heterozygous CRZ knockout females (+/ΔCrz), and we clarify the genetic nature of the knockout as follows:

(1) Genetic basis of the CRZ knockout:

The CRZ knockout line was generated via CRISPR-Cas9-mediated deletion of the Crz coding region, resulting in a recessive loss-of-function mutation. Homozygous knockout females (ΔCrz) exhibited the full phenotypic suite reported in the manuscript (impaired post-mating suppression of remating, reduced oviposition rate, and disrupted CRZ signaling in the reproductive tract).

(2) Phenotype of heterozygous females:

Behavioral and physiological assays of +/ΔCrz heterozygotes revealed no significant differences compared to wild-type (+/ΔCrz) females across all measured post-mating traits. Specifically:

Remating rates of +/ΔCrz females were indistinguishable from wild-type controls at 48 h post-mating.

Oviposition output of +/ΔCrz females matched wild-type levels over a 3-day assay period.

(3) Updates to the manuscript:

We have added these heterozygote data as figure1J and K in the revised manuscript, with corresponding descriptions in the Results and Methods sections. We have also explicitly noted the recessive nature of the Crz mutation in the Genetic Manipulation subsection, ensuring clarity for readers.

These results confirm that the Crz knockout phenotype is fully recessive and that one functional copy of the Crz gene is sufficient to maintain normal post-mating responses—supporting our conclusion that CRZ signaling is required for mediating female PMR.

We thank you again for raising this important point, which has strengthened the genetic rigor of our study.

(13) Figure 1, Supplementary 1: I do not understand why the authors point out the fact that these are Protostomia. These are all Arthropoda, there is not a single species outside this Phylum. Caerostris darvini should be Caerostris darwini.

Thank you for this feedback regarding Figure 1 and Supplementary Figure 1. We fully agree and have addressed these issues in the revised manuscript:

(1) Removal of the "Protostomia" designation

We have deleted all references to Protostomia from the figure legends and associated text.

(2) Spelling correction of Caerostris darwini

We apologize for the typographical error in the species epithet. We have corrected the misspelling Caerostris darvini to the taxonomically accurate Caerostris darwini (Darwin's bark spider) across all instances in Figure 1, Supplementary Figure 1, and their corresponding legends. We have also cross-checked all other species names in the manuscript to eliminate similar typographical errors.

(14) Line 299: CRZ expression: I found this confounding, given that the authors were talking about the expression of the gene. I would use the term localization, referring to the protein/peptide (is it what the authors were pointing at?).

To resolve this ambiguity, we have revised Line 299 to replace CRZ expression with CRZ peptide localization, which accurately describes the experimental focus (immunofluorescence staining and confocal imaging of the CRZ protein). We have also cross-checked the entire manuscript to standardize this terminology:

We use Crz gene expression exclusively when referring to transcriptional analyses (e.g., qRT-PCR results).

We use CRZ peptide localization when describing the spatial distribution of the protein (e.g., immunostaining assays).

(15) Figure 2C: The expression is relative to...? I would make it explicit on the axis.

Thank you for this helpful comment. We apologize that the normalization reference was not sufficiently clear in the original version. In the revised manuscript, we now explicitly state that RT–qPCR data were first normalized to the reference genes Actin and 18SrRNA, and then expressed relative to the mean expression level of the tissue showing the highest Crz expression, which was set to 1. We have clarified this information in the figure legend and the Methods section.

We have revised Figure 2C as follows:

Updated the Y-axis label to explicitly state the reference: “Relative Crz gene expression”.

Added a supplementary note in the figure legend to confirm that relative expression values were calculated using the 2^⁻ΔΔCt method, with the reference gene serving as the internal control for normalization.

Additionally, we have cross-checked all other qRT-PCR-related figures in the manuscript to ensure that the reference for relative expression is clearly indicated on the corresponding axes, standardizing this key detail across all gene expression datasets.

(16) Figures 3B, E, I, L, M, N: Percentage and proportions, as in Figure 1; furthermore, please provide the minimum number of individuals per replicate. Furthermore, as in Figure 1, the data are proportions, and I would use statistical tests that are studied for this kind of data.

Thank you for this helpful suggestion. We have reviewed and corrected the Y-axis labels and corresponding numerical ranges in these figures, and we have added the number of replicates and the minimum number of individuals per replicate to the figure legends. In addition, following your recommendation, we have reanalyzed these proportion data using chi-square tests for contingency tables.

(17) Figure 3: As in Figure 1, it would be interesting to know which is the behaviour of the heterozygotes.

Thank you for suggesting to complement the data in Figure 3 with heterozygote phenotypic analyses.

To address this, we have conducted additional behavioral and physiological assays of heterozygous CrzR knockout females (+/CrzR^M) and integrated these data into the revised Figure 3 and its legend:

Phenotypic characterization of heterozygotes: Across all traits measured in Figure 3 (e.g., remating rate and oviposition efficiency,), +/CrzR^M females exhibited no significant differences compared to homozygotes.

This confirms that the CrzR knockout phenotype is dominant and that one functional copy of the CrzR gene can’t to maintain normal post-mating response (PMR).

Manuscript updates:

We added heterozygote data in Figure 3I and J. Accordingly, we updated the Results text to reflect the revised panel labeling.

We supplemented the figure legend with statistical comparisons between heterozygotes and wild-type groups (using chi-square tests for proportional data).

We included a brief description of heterozygote phenotypes in the Results section to contextualize the genetic basis of the CrzR-mediated PMR regulation.

(18) Figure 3 Supplement 1: Can the authors indicate which model for maximum likelihood they chose? Did they perform a pre-test to assess which substitution model was the best for their data?

Thank you for this critical question regarding the model selection for maximum likelihood (ML) phylogenetic analysis in Figure 3 Supplement 1. We fully agree that specifying the substitution model and validation process is essential for ensuring the reproducibility and rigor of phylogenetic inferences.

To address this, we have supplemented the manuscript with detailed information on the model selection and validation steps, as follows:

(1) Substitution model selection

Prior to constructing the ML tree, we performed a model selection pre-test using the ModelFinder tool integrated in IQ-TREE 2, which evaluates the fit of candidate nucleotide substitution models to the CrzR amino sequence alignment via the Bayesian Information Criterion (BIC). The model selection procedure identified the LG+G model as the best-fit substitution model for our dataset. This model uses the Le and Gascuel (LG) amino-acid substitution matrix and incorporates a gamma-distributed rate variation among sites (G) to account for among-site rate heterogeneity.

(2) Manuscript updates

We have added this detailed model selection process and the final LG + G model specification to the legend of Figure 3 Supplement 1.

We have also included information on bootstrap validation (10000 ultrafast bootstrap replicates) to support the node support values reported in the phylogenetic tree.

(19) Figure 4 Supplement 1: I would be explicit about what it is relative to (which gene).

Thank you for this helpful comment, In the revised manuscript, we now explicitly state that RT–qPCR data were first normalized to the reference gene Actin, and then expressed relative to the mean expression level of the tissue showing the highest CrzR expression, which was set to 1. This normalization strategy provides a robust and biologically representative reference. We have clarified this information in the figure legend and the Methods section.

(20) Line 518 and Line 525 and Figure 5: The authors show that injection of CRZ and RNAi of crz or mutant crz has the same effect on male fitness. How do the authors explain this contradiction? The CRZ injection should activate the pathway, and crz RNAi and mutant crz should inhibit the pathway, but nevertheless, they have the same effect. I would probably test the expression of some of the genes whose expression is altered in crz mutant males (next paragraph) to see if an altered CRZ signalling pathway (both ways) might affect gene expression in the MAGs in the same way.

Thank you for raising this important point. As explained above, we have removed all data related to CRZ function in male BPHs from the current version.

(21) Figure 5, Figure 7: As in Figures 1 and 3, please pay attention to the percentages and proportions and the statistical tests.

Thank you for pointing out these issues. We have carefully reviewed and corrected the percentage/proportion labeling in the relevant figures, including the Y-axis descriptions and numerical ranges, as well as revised the corresponding figure legends. In addition, we have reanalyzed the data using statistical tests appropriate for proportion data. All corresponding revisions have been incorporated into the updated manuscript.

(22) Line 728-745: As already stated for the abstract, the male effect of crz is, to me, a side product, and I am not sure the male crz signalling has something to do with the female crz signalling. It is interesting, nobody showed that CRZ affects expression in the MAGs, but this is not the main message of the paper, and it confuses the reader. I would reduce the discussion about this aspect and move it to the end, but this is my own take.

We have removed all data related to CRZ function in males for the reasons outlined above.

(23) Material and methods/results: as a general suggestion, I would be explicit about the timing of receptivity inhibition in the species. I've seen the authors have established this in precedent work, and I would refer to that work and make the reader aware of how the receptivity works in the species (i.e., that it is not permanent and lasts for a few days after first mating). This allows a better understanding of the experimental design.

Thank you for this valuable and constructive suggestion. We fully agree that explicitly describing the timing of receptivity inhibition in Nilaparvata lugens, and linking it to our earlier work, will strengthen the rigor and clarity of the manuscript.

To address this, we have revised the Materials and Methods and Results sections as follows:

(1) Materials and Methods (Experimental Design subsection)

We have added a dedicated paragraph that explicitly defines the temporal dynamics of post-mating receptivity inhibition in N. lugens, with direct reference to our prior work[1]. The text clarifies:

“In N. lugens, mating induces a transient suppression of female receptivity that is not permanent. Females typically start regain remating willingness 72 h after the first mating, as documented in our previous study[1]. This temporal window guided the design of our remating assays, in which females were paired with naive males at 48 h post-initial mating to capture both the suppressed and recovered phases of receptivity.”

(2) Results (Post-mating Receptivity section)

We have incorporated a brief contextual sentence at the start of the section to reinforce this key species-specific trait, ensuring that readers connect our assay timings to the temporal dynamics of receptivity in N. lugens.

These revisions ensure that the rationale behind our experimental timing is transparent and well-supported, allowing readers to fully grasp how our assays were tailored to the biological characteristics of N. lugens.

(24) Line 854: There is a typo "CRZ peptide. virgin female", the dot should be a comma.

We have revised Line 854 to correct the punctuation: the dot has been replaced with a comma, resulting in the phrasing "CRZ peptide, virgin female". In addition, we have changed the wording in this sentence to ensure scientific rigor and to avoid colloquial expressions.

(1) Zhang, Y.J., Zhang, N., Bu, R.T., Nässel, D.R., Gao, C.F., and Wu, S.F. (2025). A novel male accessory gland peptide reduces female post-mating receptivity in the brown planthopper. Plos Genet 21, e1011699. 10.1371/journal.pgen.1011699.

eLife Assessment

This study addresses an important question about how large-scale brain networks interact, and specifically how the default mode network exchanges information with the sensory cortex. The analyses are sophisticated, but at present provide incomplete evidence for the claims made in the paper.

Reviewer #1 (Public review):

Summary:

This paper leverages 7T fMRI data from the Natural Scenes Dataset to investigate whether retinotopic coding, the position-selective organization of visual response structures, spontaneous resting-state interactions between the Default Network (DN) and the Dorsal Attention Network (dATN). Using individualized network parcellations and population receptive field (pRF) modeling, the authors show that DN voxels can be split into two subpopulations based on their response to visual stimulation: those with position-specific positive BOLD responses (+pRFs) and those with position-specific negative BOLD responses (-pRFs). Critically, these subpopulations relate differently to the dATN during rest: -pRFs are anticorrelated with the dATN, +pRFs are positively correlated, and non-retinotopic DN voxels show no coupling. The anticorrelation (and positive correlation) is enhanced when DN and dATN voxels share visual field preferences. An event-triggered analysis suggests that retinotopic coding shapes both "top-down" (DN-initiated) and "bottom-up" (dATN-initiated) spontaneous activity transients, supporting the claim that the retinotopic scaffold is intrinsic to the DN. These findings challenge the prevailing view of global DN-dATN antagonism and suggest retinotopic coding as an organizing principle for cross-network communication.

Strengths:

The central finding that what looks like network-level independence between DN and dATN decomposes into structured, bivalent interactions organized by voxel-level visual field preferences is a compelling demonstration that macro-scale network descriptions can hide meaningful substructure. The logic of the analysis is clean: pRF properties are estimated from retinotopic mapping data and then used to predict resting-state coupling in completely independent scanning sessions. This cross-session, cross-modality design rules out many circularity concerns.

The use of individualized multi-session hierarchical Bayesian parcellation (Kong et al.) to define DN and dATN boundaries within each subject is the right methodological choice for this question. Network boundaries in posterior cortex, where DN and dATN interdigitate most closely, vary considerably across individuals, and group-average approaches would introduce exactly the kind of misassignment that would most confound the result.

The matched-vs-random pRF analysis is well-controlled. The authors demonstrate that cortical distance between matched and randomly-matched dATN pRFs does not differ, effectively ruling out spatial proximity on the cortical surface as a confound. tSNR controls further show that signal quality differences do not drive the effect.

The event-triggered analysis (Figure 3) is creative and adds genuine value. Showing that retinotopically-specific coupling persists during DN-initiated activity transients, not only dATN-initiated ones, is the key piece of evidence for the claim that the code is intrinsic to the DN rather than passively inherited through bottom-up visual drive.

The result is observed consistently across all individual participants, which provides strong evidence for the robustness of the qualitative pattern despite the small sample size inherent to densely-sampled designs.

Weaknesses

(1) The nature of negative pRFs requires more scrutiny

The entire interpretive framework depends on treating negative pRFs in the DN as genuine position-selective neural responses (suppression). However, negative BOLD signals are well known to arise from non-neural sources, specifically, vascular stealing (where activation in nearby tissue diverts blood from adjacent voxels) and macrovascular draining vein effects that produce spatially displaced signal inversions. These concerns are amplified at 7T, where T2*-weighted GE-EPI carries substantial macrovascular weighting. The DN and dATN interdigitate extensively in the posterior cortex, often within millimeters. A negative pRF in a DN voxel adjacent to a positive dATN voxel could, in principle, reflect the hemodynamic shadow of its neighbor rather than an independent neural response.

The spatial dispersion control (matched vs. random pRFs have similar cortical distribution) is valuable but addresses long-range confounds, not *local* hemodynamic crosstalk. The reliability of sign and center position across runs is reassuring but does not exclude a vascular origin, as vascular architecture is itself stable across sessions. I would encourage the authors to test whether the matched-vs-random effect survives exclusion of voxels near large pial vessels (identifiable from T2* contrast or the venograms available in the NSD). These analyses would not be dispositive, but they would meaningfully strengthen the neural interpretation.

(2) Amount of retinotopic mapping data and choice of pRF pipeline

The NSD includes 6 runs of retinotopic mapping (~5 minutes each; 3 bar-aperture, 3 wedge/ring). The authors use only the 3 bar-aperture runs (~15 minutes total per subject) and fit their own pRFs using AFNI's 3dNLfim procedure, rather than using the pRF estimates provided as part of the NSD release (which were fitted using the analyzePRF toolbox with all 6 runs).

Fifteen minutes of bar data is quite limited for reliable voxel-wise pRF estimation, especially in regions far from the early visual cortex, where signal-to-noise is inherently lower. Standard recommendations for robust pRF mapping in higher-order regions generally suggest substantially more data. The variance-explained threshold is close to the noise floor by design, meaning that a non-trivial number of the "retinotopic" DN voxels may be poorly estimated. Given that the core analyses depend on both the sign and the center position of these pRFs, the limited data is a significant concern.

The authors do not explain why they chose to re-fit pRFs rather than use the NSD-provided estimates. If the motivation was methodological (e.g., the NSD pRF pipeline does not readily yield signed amplitude, or the bar-only fits were judged more appropriate for detecting negative responses), this should be made explicit. If the NSD-provided pRFs can reproduce the key findings, this would substantially increase confidence in the results. If they cannot, that divergence itself would be important to understand. I would ask the authors to address this choice and, if feasible, to report whether the core results replicate using the NSD-provided pRF estimates and/or whether using all 6 runs of retinotopy data changes the findings.

(3) pRF model adequacy for the Default Network

The isotropic Gaussian pRF model was developed for and validated in early and mid-level visual cortex, where it captures the dominant spatial selectivity of neuronal populations. In DN voxels where the model explains comparatively little variance, it is less clear that the model is capturing the right quantity. Specifically, the negative pRFs could conceivably be described by a model with a dominant suppressive surround (e.g., a difference-of-Gaussians model), in which what appears as a "negative pRF" in the standard model is actually the surround component of a center-surround mechanism whose center is poorly resolved. This distinction matters: a genuine inverted code (negative center response) implies a qualitatively different computation than inherited surround suppression from nearby visual cortex.

The authors should consider discussing why the standard model is sufficient for the questions asked, or ideally, testing whether the sign distinction survives under alternative pRF model specifications.

(4) Interpreting resting-state transients as top-down vs. bottom-up

The event-triggered analysis labels high-amplitude DN pRF activations as "top-down events" and dATN activations as "bottom-up events." This is a reasonable inference given experience-sampling studies showing that rest involves alternation between internal and external attention, but it remains an inference. Without concurrent experience sampling, eye-tracking, or physiological monitoring, we cannot establish that a spontaneous DN transient reflects memory retrieval or internally-directed thought rather than a global arousal fluctuation. Similarly, dATN transients during rest could reflect covert shifts of spatial attention to remembered or imagined locations rather than bottom-up processing per se. I would ask the authors to soften this framing or to discuss what additional data would be needed to validate the top-down/bottom-up attribution.

(5) The "retinotopic code" vs. "visual field bias" distinction

The paper uses the language of a "retinotopic code" throughout and correctly distinguishes this from a "retinotopic map," noting that DN voxels do not form a continuous topographic representation on the cortical surface. This distinction deserves greater emphasis. In vision science, retinotopic maps carry computational significance through their topographic continuity and relationship to cortical wiring. A distributed collection of voxels with coarse visual field preferences but no cortical topography is a fundamentally different organizational feature. Recent reviews have drawn an explicit distinction between *retinotopic maps* and *visual field biases* (Groen, Dekker, Knapen & Silson, TiCS 2022), and the present findings may be more accurately characterized as the latter. Perhaps the authors think that the distinction is merely a signal-to-noise distinction, in which case I would invite them to clearly speak to this interpretation. In any case, this is not a criticism of the findings themselves, but clarity on this point would prevent conflation of two different organizational principles and would help position the work for both the vision and network neuroscience communities.

Reviewer #2 (Public review):

Summary:

Using a public dataset of retinotopic mapping and resting-state data, the authors find that the default mode network has voxels that respond (positively or negatively) to visual stimulation at specific retinotopic positions, and that resting-state activity in these voxels is correlated with activity in more traditional sensory voxels with the same visual-location preference. The retinotopic specificity is bidirectional, such that high activity in default mode voxels drives activity only in voxels with matching receptive fields in sensory cortex, and vice versa. These findings are at odds with traditional views of the default mode network as having abstract (non-retinotopic) representations and competing (rather than cooperating) with external sensory representations.

Strengths:

This study continues an intriguing line of research about how default mode regions interact with the sensory cortex. Demonstrating that there are structured interactions between these regions at rest, and that these interactions are in fact organized according to retinotopic location (as opposed to traditional views of representational format in the default mode network), provides a new framework for thinking about large-scale internal and external brain networks. The authors make use of a well-powered public dataset that allows for precise estimates of pRFs and individual-specific resting-state networks, and develop a number of interesting analyses that characterize the relationships between DN and dATN voxels. The findings are exciting and could have a major impact on future studies in cognitive neuroimaging.

The authors mention that these findings could shed light on internal/external interactions such as "anticipatory saccades or memory-guided attention," which is true, though I would argue that constructing DN representations of external stimuli is in fact even more fundamental than these specific cases (e.g., see Barnett and Bellana, 2025, "Situation models and the default mode network"). The "highways" identified in this study could play a vital role in real-world perceptual processes that are constantly translating external input into internal mental models.

Weaknesses:

(1) The criterion used for defining voxels as retinotopic seems very liberal. The authors show that only 5% of voxels have R^2>0.14 in a null analysis, and therefore define voxels with R^2>0.14 as retinotopic. Although all the networks in 1C show voxel distributions that differ from the null, the number of false positives above R^2>0.14 seems problematic, especially for the DN positive pRFs (red distribution) and to a lesser extent the DN negative pRFs (blue distribution). From visual inspection of the plot, the false discovery rate (fraction of voxels labeled as retinotopic that are false positives) looks like it would be greater than 50% for the DN-positive pRFs. The authors do show that the positive pRF voxels have above-chance consistency across runs, again providing evidence that there are true positive voxels in this set, but perhaps a stricter criterion (such as having consistent negative fits across runs) would provide more targeted identification of the DN voxels with true retinotopic sensitivity.

(2) The claim that "opponency at rest between the DN and dATN appears to be driven by the subset of DN voxels with negative retinotopic tuning" is not well supported. The fraction of DN voxels with negative pRFs is small: 9.42% of DN voxels have pRFs, and 58.77% are negative, so about 6% of DN voxels have negative pRFs. The fact that any DN voxels have negative pRFs is notable, but the authors do not provide evidence that these 6% are driving the overall behavior of the DN. They do show (e.g., in Figure 2B) that negative and positive pRFs have opposing influences, but the overall correlation with dATN does not look similar to the negative pRF connectivity. I'm also unsure whether "opponency" is a reasonable description for two networks that are "independent (i.e., not correlated)" in this analysis.

(3) The event-triggered analysis is effective at testing the bidirectional relationship between DN and dATN, with high activity in either network triggering a response in the other network. However, it would be helpful to show more validation that these "events" are meaningful windows of time to study. First, is 13 TRs a typical length of time that activity is elevated during one of these events? Second, the top-down and bottom-up terminology is perhaps too loaded and not well-justified; if the negative pRFs in the DN reflect a meaningful coding system, then couldn't low (rather than high) activity indicate a top-down event?

(4) The framing of this paper relative to the authors' past week, such as Steel et al. 2024 ("A retinotopic code structures the interaction between perception and memory systems"), could be improved. The existence of negative pRFs in the DN and a functional relationship between these pRFs and the sensory pRFs have already been described in prior work. My understanding of the primary novelty here is that this paper examines resting-state data, showing that there are widespread spontaneous interactions between broad internal and external networks, but this distinction is not made explicit in the Introduction.

(5) The definition of the default mode (DN) in this study aligns with past research, but the definition of the dorsal attention network (dATN) seems at odds with standard terminology. For example, the authors cite Fox et al. 2006, which depicts the dATN as including regions such as IPS, FEF, SMA, and MT+. Here, however, the "dATN" seems to be primarily lateral and ventral visual cortex (e.g., Figure S5). The exact location of these sensory pRFs is not critical to the authors' claims, but this labeling seems incorrect, and the motivation for defining/selecting the sensory network in this way is not described.

Reviewer #3 (Public review):

Summary:

This paper addresses an important question (the relationship between DN and dATN, and the role of retinotopic coding) and uses a set of novel analyses.

Strengths:

Important question, novel analytical approaches (pRF-informed functional connectivity analysis).

Weaknesses:

Some of the key claims are not fully supported by the data presented. There is also a concern about over-interpretation of the results. Key issues:

(1) The authors claim that retinotopic coding scaffolds the interaction between DMN and dATN. However, retinotopically tuned voxels account for a mere 9% of DMN voxels. So this appears to be a major overstatement. For instance, the statement that "these findings would position retinotopy as a unifying framework for brain-wide information processing" is not justified given the presented data.

(2) Given that positive pRF voxels in DMN positively correlate with dATN voxels and negative pRF voxels in DMN negatively correlate with dATN voxels, there is a concern that these results could be contributed to by imprecise brain network parcellations. E.g., could some of the positive pRF voxels in DMN be erroneously assigned to DMN and actually belong to one of the other task-positive networks? There is insufficient validation of network parcellation to put this worry to rest, especially since it depends on ICA, which has a degree of arbitrariness built in.

(3) The claim that retinotopic coding is intrinsic to the DN network is not supported by rigorous analysis and results. The analysis here has many arbitrary factors, including: the threshold of the 99th percentile of resting-state distribution; the designation of DN as "top-down" and dATN as "bottom-up"; the definition of "anti-matched" voxels instead of using randomly selected voxels; and the statistics being paired between matched and anti-matched voxels instead of using comparisons to baseline. Overall, I do not think that the result supports the conclusion that retinotopic coding in DN is intrinsic instead of being bottom-up-driven, given the very high threshold (99%) used and the fact that many other networks could also send bottom-up input to DN. Furthermore, the idea that bottom-up inputs only occur when the dATN (or any other RSN)'s spontaneous BOLD activity is above a certain threshold is a huge and unvalidated assumption.

eLife Assessment

This important study addresses a discrepancy between population-level growth laws and single-cell correlations. It shows, for flagellar and synthetic genes in E. coli, that while gene expression of certain genes reduces population-average growth, expression levels positively correlate with growth at the single-cell level. The measurements are mostly convincing, and the proposed mechanism-inheritance of growth factors such as ribosomes during asymmetric division- explains this observation. The theoretical analysis would benefit from clearer explanations and robustness checks.

Reviewer #1 (Public review):

Summary:

Garcia-Alcala, Kratz and Cluzel investigate to what extent our understanding of bacterial physiology in bulk experiments can be applied to single-cell observations. They find that intrinsic noise may be powerful enough to even inverse the trends found in the bulk. The authors hypothesize that the asymmetric distribution of ribosomes to daughter cells during cell division plays the dominant role in the intrinsic noise and is able to generate the observed phenomenon. They do not show it directly, but the data and its agreement with the model are sufficient to support this claim.

Strengths:

The experimental part is convincing: the positive correlation between the elongation rate and promoter activity of unnecessary protein is clear, as well as the negative correlation between the mean values while changing the promoter strength. This was demonstrated in both rich and poor media. The causality between the growth rate and the promoter activity was shown using the negative lag time of the cross-correlation function. A simple, reasonable model accounts well for the data. This paper demonstrates an interesting phenomenon and provides a plausible theory for it, advancing our understanding of bacterial physiology on the single-cell level.

Weaknesses:

(1) Mean-reversion timescales were assumed to be longer than the simulation time and much longer than the cell cycle time. It is not clear whether the results are robust in case mean-reversion timescales become of the order of the cell-cycle or smaller. If not, is there an argument for such practically infinite reversion timescales?

(2) It is not easy to understand the simulation part unless one reads Ref. [14]. k(t) is assumed Equation (1) from Reference [14]? Is it crucial that the ribosome noise appears only at the division? The ribosome noise strength \sigma_R=0.06 - is it lower or higher than the naively expected binomial division? Also, a more intuitive explanation of the Simpson paradox would help the reader.

(3) It would be useful for the reader to see the raw data and not only the filtered one to appreciate the measurement noise level.

(4) Negative lag time of the cross-correlation function is visible, but consider adding a statistical test for it.

(5) Can you make similar cross-correlation plots using the model? Can you infer by using it, whether the data agrees better with the assumption that ribosomal noise appears only at division or continuous fluctuations during the cell cycle?

Reviewer #2 (Public review):

Summary:

The manuscript by Garcia-Alcala et al. reports an interesting paradox: the cost of gene expression slows the population-average growth rate, whereas at the single-cell level, expression levels from these genes positively correlate with the growth rate. The effect is observed in the expression of flagellar genes and a gene under a synthetic promoter in E. coli. The findings are explained by the inheritance of growth factors, including ribosomes, during asymmetric division.

Strengths:

(1) The manuscript adds strength to an emerging body of literature showing that the population-level bacterial growth laws do not match correlations based on single-cell data. The evidence presented here is more striking than in previous works (such as Pavlou et al., Nat. Commun. 2025), as the trends in population-level data and single-cell data are reversed.

(2) A relatively simple model correctly explains the trends in the data.

Weaknesses:

(1) It is not clear whether flagellar proteins are expressed proportionally to the reporter signal. Furthermore, it is questionable if E. coli bacteria in the mother machine channels are flagellated. If they are, they could potentially swim out of the channels, which is not the case when they do not carry the MotA E98K mutation. The authors should provide some evidence that E. coli expresses the actual filament proteins in the channels.

(2) It is unclear what fraction of the total proteome mVenus represents in different measurements. Some quantification is needed (for example, using the Coomassie staining). Using f_U as high as 14.4% in simulations is questionable.

(3) The data from the MC4100 strain does not directly match the trends of MG1655. The justification for filtering out the low-frequency components of MC4100 is not particularly convincing. It appears unlikely that ribosomes or other growth factors partition significantly differently in the MC4100 strain than in the MG1655 strain. Further discussion and a plot similar to Figure 1 (Left) for this strain are warranted.

(4) The model needs to be described in more detail. A closed set of equations that has been simulated must be presented, along with all values of the model parameters and their sources. The authors should consider depositing their code on GitHub or another publicly accessible repository.

eLife Assessment

This important study measures single-unit activity in the middle temporal area (MT) of awake-behaving monkeys to test the idea that sensory adaptation contributes to flexible evidence accumulation during decision-making. Solid evidence is provided, showing that adaptation to different temporal contexts shapes both perceptual judgements and neural responses, but analyses aimed at establishing a direct link between them are less persuasive. This work has the potential to be of interest to a broad range of researchers working on visual perception, plasticity, and decision making.

Reviewer #1 (Public review):

Summary:

Effective decision-making in dynamic environments requires the brain to flexibly adjust how sensory evidence is accumulated over time, a process often modeled as an adaptive "leak." McGaughey and Gold propose that this flexibility is not solely a property of downstream integrators but is also supported by stimulus-specific sensory adaptation in the middle temporal area (MT). By recording single-unit activity in rhesus macaques during a motion direction-discrimination task, the authors found that more rapidly changing environments lead to reduced sensory encoding and discriminability in MT, which they argue accounts partially for a "leakier" integration. Furthermore, the study identifies pupil-linked arousal as a parallel, independent mechanism contributing to this adaptive process.

Strengths:

The study addresses an important question in cognitive neuroscience by exploring the neural substrates of perceptual flexibility. A major strength is the novel focus on how sensory adaptation, rather than just downstream integration, contributes to behavioral changes in dynamic environments. By shifting the perspective toward the encoding stage, the authors provide a more comprehensive account of how the brain manages evidence accumulation. This conceptual advance is supported by a rigorous experimental approach that combines human-like psychophysics with large-scale single-unit recordings in the middle temporal area (MT) and pupillometry.

Weaknesses:

(1) Alternative mechanisms for performance differences

The authors assume that the difference in performance between the low-switch (LS) and high-switch (HS) frequency conditions is explained by a change in the "leakiness" of integration. However, several other mechanisms could potentially explain this effect:

(i) Temporal Uncertainty: Integration might start later in the HS condition, leading to lower performance.

(ii) Reduced Efficiency: Integration could be less efficient in the HS condition (i.e., lower signal-to-noise ratio) without a change in the leak parameter itself.

(iii)Evidence Contamination: Motion information from the adapting stimulus in the HS condition may be integrated rather than ignored, which might be the case since the transition from the adapting to the test stimulus is not externally cued.

To distinguish between these alternatives, I suggest two possible analyses. First, a formal model comparison could be performed, though I acknowledge this may be inconclusive in the absence of response-time data. Second, an analysis of motion energy kernels could be revealing; the leak hypothesis makes the specific prediction that for long test stimuli, early samples should contribute more to the choice in the LS condition than in the HS condition, relative to late samples.

(2) Independence of neural and pupil-linked signals


The authors take the lack of session-wise correlation between context-dependent contributions from neural and pupil terms as evidence that these two signals provide independent contributions to the behavioral effect. However, could this lack of correlation simply be a result of high variability or noise in these estimates? The data shown in Figure 7B suggests that measurements are very noisy, which might obscure a potential relationship.

Reviewer #2 (Public review):

McGaughey & Gold trained rhesus macaque monkeys to perform a motion-direction discrimination task in which a behaviorally irrelevant adapting stimulus with either fast or slow direction alternations preceded a variable-duration test stimulus, while simultaneously recording single-unit activity in area MT and pupil diameter. They report that adaptation to the more rapidly changing stimulus was associated with reduced behavioral sensitivity, attenuated test-evoked MT responses, and larger pupil-linked arousal signals. The authors interpret these behavioral changes as evidence for a more "leaky" evidence-accumulation process, and argue that this apparent leak is implemented in part through context-dependent sensory adaptation in MT and in part through arousal-related mechanisms. More broadly, they conclude that flexible evidence accumulation in dynamic environments arises from distributed adjustments across sensory encoding and neuromodulatory systems rather than solely from changes within a downstream accumulator. If correct, this interpretation has significant implications not only for our understanding of the neural mechanisms of perceptual decision-making but also for broader theories concerning the functional role of sensory adaptation.

The conclusions of the paper are mostly well supported by the data. Evidence for robust adaptation-induced changes in sensory encoding, behavior, and pupil dynamics is convincing, but further clarification and refinement are needed to establish a clear mechanistic link between these effects and decision-making processes.

Aspects of the behavioral analysis would benefit from a tighter connection between theoretical claims about evidence accumulation and the empirical features of the psychometric functions. For example, the rightward shifts observed across adapting conditions are interpreted as consistent with a reset of accumulation on switch trials, but similar patterns could also arise from failures to detect the test stimulus on a subset of trials, leading responses to default to the final adaptor direction. Likewise, changes in psychometric slope and asymptote are attributed to differences in evidence accumulation without explicit modelling or consideration of alternative explanations. Clarifying how specific features of the psychometric functions map onto distinct components of the decision process will strengthen the link between the theoretical framework and the behavioral data.

A slight concern is the lack of a consistent analytical approach for relating behavioral changes to neural and pupil-linked measures. Different sections of the manuscript rely on different behavioral metrics-such as differences in accuracy within a selected stimulus-duration range (e.g., Figure 5C) or psychometric slope differences (Figure 6C) - without clear justification for these choices. The analytical approach likewise varies between simple correlational analyses (Figure 5C, Figure 6C), pseudo-experimental group comparisons (Figures 5D, E), and the inclusion of neural or pupil terms in the behavioral psychometric regression model (Figure 7B). While each metric and approach may be defensible in isolation, adopting a more consistent framework will help convince readers that the reported effects are robust and not contingent on the selective choice of metric or analysis.

Reviewer #3 (Public review):

Summary:

Environments change over time; therefore, optimal decision-making ought to discount older observations of the environment in favor of newer ones in a manner consistent with the amount of temporal instability. Computational models of perceptual decision-making model this temporal discounting with a 'leak' parameter that determines the rate at which older information is discarded. In this study, McGaughey and Gold examine the neurophysiological mechanisms that could underlie adaptation to different degrees of temporal instability. They developed a novel variant of the well-established perceptual decision-making random-dot-motion paradigm, in which the stimulus being evaluated was preceded by an 'adapting' stimulus with either high or low temporal stability. When the test stimulus was preceded by the adapting stimulus with lower temporal stability, NHPs showed reduced psychometric slopes, indicative of increased temporal discounting ('leak'). While the NHPs performed this task, single-unit neural activity was recorded in area MT, along with pupillometric data. The authors use these neural and pupil datasets to investigate two potential sources of adaptive discounting under varying amounts of temporal instability: sensory adaptation (changes in instantaneous evidence encoding), and arousal-related changes in evidence accumulation. MT neurons respond differently to the test stimulus under conditions of high vs low temporal stability of the adapting stimulus - when the adapting stimulus is more stable, MT neurons have larger and more selective responses to the test stimulus. In addition, evoked pupil responses to the test stimulus were modulated by the adapting stimulus. Both the strength of the difference in MT responses across contexts and the difference in pupil diameter across contexts were correlated with context-dependent modulation of the monkeys' behavior over sessions. The paper concludes that both sources appear to independently contribute to adaptive evidence accumulation, likely operating at different processing stages in the brain.

Strengths:

(1) While computational models of perceptual decision-making have been very useful for explaining behavior and neural responses in decision-making areas, we are still in search of some of the neural mechanisms that could implement such models. Studies such as this one, which aim to identify neural correlates of simplified model parameters, are quite crucial.

(2) Analysis is generally careful and well-executed.

(3) Prompts some interesting follow-up questions that could be answered with simultaneous recordings and causal manipulations, as the authors state in the Discussion - e.g., which areas are affected by arousal-related neuromodulation correlated with evoked pupil size and how.

Weaknesses:

(1) The task design may not be optimal. While the amount of time the monkey is exposed to each motion direction during the adapting stimulus is matched, it's hard to know if the reduced MT responses to the test stimulus are truly due to the greater frequency of switches during the HSF adapting stimulus or because the monkeys have been exposed to more repetitions of the stimulus. It's increased sensory adaptation in either case, but it makes it problematic to interpret this as temporal context-dependent adaptation specifically. I think this could potentially be partially addressed by an analysis that is in the paper, but could potentially be emphasized/fleshed out more, specifically the results shown in Figure 4D that seem to show that most of the reduction in neural response for adapting units occurs between the first and second stimuli.

(2) The pupillometric analysis seems to be an indirect way of assessing whether the accumulator itself might be modulated by temporal context, but the link could be made clearer. The authors show that context-dependent behavior is related to pupil size, which is related to arousal/neuromodulation, but it would be helpful to have some idea of what neural mechanisms underlying adaptive decision-making are actually impacted by this neuromodulation. Lacking neural data to address this question (e.g., from a brain region proposed to be involved in the accumulation process), at least more discussion of this would be helpful. Essentially, I'm unsure of how to interpret the pupil results: the argument that temporal context affects instantaneous evidence encoding in MT that then drives the accumulator is very clear, but I am a bit confused about what, mechanistically, I should think about the effect of neuromodulation doing.

eLife Assessment

The valuable study aims to differentiate between foveal and peripheral attentional mechanisms in visual and frontal brain regions in monkeys engaged in a free-gaze visual search task. The authors interpret differences in responses between target and nontarget conditions as feature-based attention; however, this may not be the correct interpretation. The authors do not provide enough information on how they distinguish foveal and peripheral RFs. Consequently, the study provides only incomplete evidence that does not support the authors' conclusions, and the significance of the findings is not strong.

Reviewer #1 (Public review):

Summary:

This manuscript aims to differentiate between foveal and peripheral attentional mechanisms in visual and frontal brain regions in monkeys engaged in a free-gaze visual search task.

Strengths:

The manuscript is clearly written, the question is important, and the behavioral task is interesting.

Weaknesses:

I have two major concerns.

(1) The authors interpret divergence in neural responses to target vs nontarget as attention. But it is not. The subject has to attend to both target and nontarget stimuli to determine the stimulus category and thereby decide on the next action. Thus, divergence between target and nontarget responses could reflect categorical discrimination, but I am not sure this can be interpreted as attentional modulation. While it may be tempting to suggest that finding a stimulus of a specific category is "feature attention", analogous to, e.g., attending to the red stimulus, I don't believe this is correct. For the former, the animals have to attend to a stimulus, and examine the stimulus to determine the stimulus category, unlike a simpler discrimination, which may pop out. Given this, I am unconvinced that the interpretations in this manuscript are valid.

(2) Regarding the RF classification of foveal and peripheral RFs for IT and PFC, prior work suggests that neurons in IT cortex (especially AIT) and PFC have RFs that largely include the foveal visual field. So, it would be important to include figures that show the RFs of neurons classified as foveal versus peripheral for all three areas.

Reviewer #2 (Public review):

Summary:

In natural visual behavior, such as when one is looking for a face in the crowd, the eyes are moved from site to site, seeking possible matching targets. This involves attention both to the current view at the center of vision (the foveal location) as well as to upcoming views via attention to targets in the periphery. While it has been established that attention generally enhances neuronal response (compared to simple visual activation) at the attended spatial location, this study provides solid evidence that attention during active visual search leads to neuronal response enhancement only when the eye moves towards targets that exhibit the desired feature and category. This study thus moves the field towards understanding the neural encoding of active vision.

This study examines the neuronal basis of feature-selective attention during active, freely behaving visual search. Traditional electrophysiological studies on visual attention in monkeys commonly used an eye fixation with a covert attention paradigm, but have not sufficiently addressed the roles of both foveal and peripheral attention in play during natural looking behavior. Here, the authors present a novel paradigm in which, during eye-movement mediated search, neuronal receptive fields are recorded in multiple cortical areas (sensory V4, temporal, and prefrontal areas). In this manner, as the eye foveates, items in the array fall into foveal or non-foveal recorded sites. Thus, the experimental paradigm is elegant, offering the opportunity to make multiple types of comparisons: target/distractor, towards/away from fovea, and areal. Specifically, following a category cue (face, house, hand, flower), freely initiated saccades are made to locate a categorically matching 'target' in an array of distractors. Feature attention is assessed by comparing eye saccades made to targets vs to distractors. Spatial attention is assessed by comparing saccades made 'towards' vs 'away' from targets. Statistics are rigorous and nicely designed. The detailed association of simultaneously obtained eye movement sequences and neural parameters is well done. These are valuable data that will contribute to our understanding of attentional modulation in visual search.

Strengths:

The significance of these findings is fundamental. Decades of attention research in vision have been based on the paradigm of visual fixation and covert peripheral attention. However, increasingly, the field has moved towards understanding how the visual system works during active vision. Here, the authors use an active visual search paradigm and record from multiple areas (V4, IT, PFC). They find enhancement of attention both in the foveal and peripheral locations, and, furthermore, a high degree of feature and categorical specificity. This provides valuable data for the concept of a foveal-peripheral attentional window in natural vision. The controls (comparisons of neuronal response during looks to targets vs distractors, and looks towards and away from the target) and statistical rigor make these findings quite compelling.

Weaknesses:

While the study is generally quite strong, there are a few weaknesses to be addressed.

(1) Little rationale is provided for recording in the selected areas, V4, IT, and PFC. Given the respective roles in sensory, object recognition, and goal-directed behavior, some rationale for this design should be offered, and commonalities/distinctions between these areas should be discussed.

(2) Given the reliance of all analyses on saccadic behavior (towards target/distractor, towards/away from target), additional description and summaries of eye movement behavior during single trials and across trials should be provided.

(3) The dependency of findings on top-down (categorical & feature-specific) task design should be discussed.

Reviewer #3 (Public review):

In this manuscript, the authors investigate the role of attention in foveal processing during a naturalistic task. They record neural activity from extrastriate visual areas V4 and inferotemporal cortex, as well as from the lateral prefrontal cortex, in macaques performing a free-gaze visual search task. In this task, animals searched for a face or house target among multiple complex stimuli, with no constraints on eye movements. Unlike classic studies of visual attention, which often rely on controlled fixation, this work examines neural activity in both foveal and peripheral receptive fields during naturalistic eye movements.

The main question addressed by the authors is how feature-based attention is distributed and coordinated across foveal and peripheral visual fields during active search, and how this attentional processing influences saccade behavior. The authors show that foveal units in visual areas exhibit feature-based attentional enhancement, with stronger responses when a fixated stimulus is a target compared to when the same stimulus serves as a distractor. Peripheral units in visual and prefrontal areas show both feature-based and spatial attentional modulation, consistent with prior work. Finally, the authors show that attentional modulation depends primarily on stimulus category rather than response magnitude, with neurons showing similar enhancement for all images within the target category regardless of how strongly individual images drive the cell.

There are several notable strengths of this paper, including:

(1) Disentangling feature-based and spatial attention during naturalistic vision remains a central challenge. This paper tackles both simultaneously, parsing neural populations by object selectivity (face-selective, house-selective, non-selective) and RF position (foveal vs. peripheral).

(2) The unconstrained search task (Figure 1A) moves beyond the dominant fixed-gaze, cued-attention designs (Zhou & Desimone, 2011) to study attention as it operates during natural behavior, with sequential fixations and voluntary saccades.

(3) The scale of the multi-area recordings is a major strength and is well aligned with current trends in primate and human neuroscience toward large-scale, multi-area recordings. Simultaneous recordings from visual and prefrontal areas, comprising over 4,900 foveal units and more than 1,500 peripheral units, enable meaningful cross-area latency comparisons and area-specific analyses of attentional modulation. This study builds on the authors' previous analyses of this dataset by expanding the scope to show that feature-based attention generalizes across neuronal classes and operates on categorical identity rather than response magnitude.

(4) The combination of simultaneous multi-area recordings and a rich behavioral paradigm provides a dataset that is well-suited for population decoding, cross-area interaction analyses, and trial-by-trial prediction of saccade choices, which could substantially deepen mechanistic understanding beyond the largely univariate comparisons presented here.

While the data broadly support the paper's main conclusions, several issues limit the strength of the mechanistic interpretation and should be taken into consideration:

(1) Receptive field size is not explicitly quantified and may confound foveal-peripheral comparisons. Units are classified as foveal or peripheral based on responsiveness to the cue versus the search array (Methods, p. 17), but the manuscript lacks essential information about receptive field sizes, eccentricities, and the number of search stimuli falling within each receptive field and related proper controls. This is critical because receptive fields in visual area V4 at foveal eccentricities are relatively small (Gattass et al., 1988; Desimone & Schein, 1987), whereas receptive fields in inferotemporal cortex can span several degrees to tens of degrees and often include the fovea (Op de Beeck & Vogels, 2000; DiCarlo & Maunsell, 2003; Zoccolan et al., 2007). Given the 2{degree sign} × 2{degree sign} stimulus size, multiple search items could potentially fall simultaneously within peripheral receptive fields. This introduces a potential confound, as attentional modulation is known to be strongest when multiple stimuli appear within a single receptive field (Reynolds et al., 1999). Although the authors acknowledge this issue for visual area V4 (p. 17), it is neither quantified nor controlled for. Without explicit receptive field mapping relative to the search array, comparisons between foveal and peripheral units, as well as between visual areas, are difficult to interpret cleanly.

(2) Attentional modulation is difficult to dissociate from saccade planning and decision-related signals. The free-gaze paradigm enhances ecological validity but introduces a temporal confound: mean distractor fixation durations are approximately 156 ms (p. 9), while attentional effects emerge between 137 and 170 ms after fixation onset (Figure 2). As a result, the reported attentional modulation coincides with the preparation of the subsequent saccade. Neural activity measured in the primary analysis window (150-225 ms; p. 19), therefore, likely reflects a mixture of visual, attentional, motor planning, target recognition, and behavioral relevance signals, all of which are known to modulate responses in visual areas at similar latencies (e.g., Chelazzi et al., 1998). Moreover, target fixations (~257 ms) and distractor fixations (~156 ms) occur on fundamentally different behavioral timescales, which may inflate apparent foveal attentional effects. While the authors suggest that these timing differences support the idea that foveal feature-based attention facilitates prolonged fixation on target stimuli, this interpretation is not fully supported by the current analyses. That said, the saccade-aligned analyses of peripheral units (Figure S3) partially mitigate this concern by demonstrating that feature-based modulation persists through saccade execution.

(3) The "attention-out" condition for spatial attention lacks directional control. In the spatial attention analyses (Figures 4D-F), the "attention-out" condition appears to include all fixations followed by saccades directed away from the receptive field, regardless of saccade direction. This differs from classic spatial attention designs, which typically use controlled anti-saccades or saccades to fixed locations opposite the receptive field (e.g., Moore & Armstrong, 2003; Gregoriou et al., 2009). Saccades directed toward locations adjacent to, but outside, the receptive field may still partially engage spatial attention mechanisms near the receptive field via broad attentional fields or motor preparation gradients (Bisley & Goldberg, 2010). In addition, the "attention-out" condition likely contains a heterogeneous mixture of trials in which the stimulus in the receptive field is either a target or a distractor, since feature-based attention effects are derived from this same pool of trials. As a result, spatial and feature attention effects are not fully orthogonal, and variance related to feature attention may already be embedded in the spatial attention baseline.

eLife Assessment

This valuable study introduces a new framework for improving the automated sorting of extracellular action potentials. However, the evidence is incomplete; the biophysical model used for simulation is based on one simulation that does not necessarily reflect real experimental data, the test datasets are insufficiently diverse, and essential algorithmic details are currently missing. This work will be of interest to neuroscientists using high-density multichannel electrophysiology.

Reviewer #1 (Public review):

Summary:

This work presents a flexible spike-sorting framework that allows users to run, swap, and benchmark individual modules commonly used in spike sorting. The paper argues and demonstrates that "opening the black box" is essential for understanding which components drive performance differences and for making progress toward more accurate and transparent spike sorting.<br /> Using this modular benchmarking pipeline, the work identifies electrode drift as a primary bottleneck for accurate sorting and introduces an end-to-end sorter ("Lupin") that combines the best-performing modules and is reported to outperform existing spike-sorting packages on their benchmark.

Overall, this is a strong tool/resource contribution with clear potential to accelerate spike-sorting development and enable more rigorous comparisons. However, several claims, particularly around Lupin's or individual modules' superiority, are not yet supported robustly enough for the strength of the conclusions stated.

Strengths:

This work has high community value and practical utility. The effort to make benchmarking and spike sorting modules accessible and standardized is substantial and likely to be broadly useful.<br /> Treating spike sorting as a set of interchangeable modules is a useful approach to some extent, and it enables targeted improvements rather than 'new sorters' popping up, which are difficult to fully understand.

Implementing this resource within SpikeInterface, an already widely used tool, will facilitate uptake and community contributions.

Overall, I am positive about this manuscript as a resource paper. The core framework is compelling and timely.

Weaknesses:

(1) The main concern is the limited support for the claim that 'Lupin' and individual modules' outperform existing spike sorters.

(2) Evidence is primarily from a single benchmark based on an intentionally simplified simulation. While the authors discuss the trade-offs between simulated and real data, the current evaluation does not provide enough diversity to justify claims of superiority.

(3) While improving individual modules that run in a serial fashion could aid overall spike sorting performance, acknowledging that some end-to-end sorters work in an iterative fashion across multiple of these modules would be fair. Perhaps the optimal spike sorter is not a serial set of modules.

(4) There is also a risk of benchmark overfitting. A modular approach makes it easy to select components that excel on specific benchmarks (or a specific project's data characteristics) without generalizing.

Concrete ways to strengthen this work:

(1) Evaluate on multiple simulation regimes, consider adding at least one biophysically detailed simulation, benchmark on multiple probe-geometries with neurons also clustered in different depth profiles (as this will affect drift solutions), and provide real-data validation. Even without full ground truth, real-data can be evaluated with expert curation, functional validation (e.g., refractory violations, quality metrics, unit waveform consistency), agreement across sorters, and consistency across time.

(2) Related to real-data applicability, it is also important to acknowledge that modulatory approaches can enable overfitting to the needs of individual projects. Without real-data benchmarking (or benchmark diversity), it is unclear how the framework will guide users towards generalizable 'best practices' rather than optimized configurations that work for their specific conditions.

Reviewer #2 (Public review):

Summary:

Spike sorting, that is, assigning events detected in extracellular electrophysiology data to the firing of individual neurons, is an inherently difficult computational problem involving multiple steps. The difficulty arises from low signal-to-noise, instability in signal due to the relative motion of the tissue and recording sites, and large volumes of data. Experimental ground truth data - where the correct assignment of spikes is known - is not available in large enough quantities to test algorithms. This paper describes a tool for creating fully synthetic ground truth data and benchmarking the individual steps of spike sorting to dissect the impact of signal-to-noise, firing rate, and motion correction on each step. This information is used to construct an optimized algorithm for sorting the ground truth data. One result of particular interest is the dominant role of motion correction in degrading accuracy. Another important technical result is that motion correction via interpolation of the voltage traces yields similar accuracy to interpolation of the spike templates.

Strengths:

The paper clearly shows the benefits of analyzing the complex process of spike sorting step by step. While this analysis has also been done in papers presenting spike sorters (for example, reference [32]), the tools presented here allow users and developers to do similar studies for their own work. This toolset will be very useful to many labs, especially those working in less studied brain areas or model systems, cases where the tuning of standard spike sorting tools is not a good match to the data.

Weaknesses:

The model ground truth data used in the paper does not need to be a perfect match to experimental data to provide useful benchmarking. However, as with all measurements of spike sorting accuracy, extrapolation to experimental data can be complicated. Users of these tools will need to assess how well the simulated data matches their recordings.

Reviewer #3 (Public review):

Overview:

In this manuscript, the authors describe two additions to an existing toolbox (SpikeInterface, Buccino et al., 2020, eLife). The first addition is an empirical simulator for extracellular recordings, in which spikes from predefined templates are added up with Gaussian noise. The second addition involves granting user-level access to intermediate processing steps along spike sorting algorithms. The authors demonstrate the toolbox by evaluating functions (e.g., event detection) or sets of functions (e.g., feature extraction + clustering) on their simulated data, and suggest that a specific combination of function implementations provides performance improvement relative to kilosort4 (Pachitariu et al., 2024, Nature Methods).

If the authors are interested in making this manuscript a suitable scientific contribution, the entire work has to be revised extensively. In particular, the simulator has to be extended and improved; the implementation of existing spike sorters has to be improved; the feedforward architecture of the modules has to be extended; the reporting of results has to follow standard reporting standards; new algorithms have to be explained in sufficient detail; and the manuscript has to undergo extensive proofreading.

Notably, even assuming perfect implementation and descriptions, it is unclear to me whether the scope of the present work warrants a publication in a scientific journal, or is more suitable for an internal technical report or an e.g., a GitHub version release. To go beyond a scientifically-sound technical report, the authors may choose to demonstrate the utility of their new proposed sorter ("Lupin") and compare it to existing tools on multiple datasets.

General comments:

(1) The simulator itself has to be improved and extended. Right now, it simply generates, for every unit, a mother waveform from a sum of exponentials, scales that over channels, and then adds up multiple instantiations of every unit on every channel, along with noise. This is not a biophysical simulator: it is an ad hoc procedure, and the sentence "we firmly believe that.." (lines 482-483) does not make the procedure convincing. To make the simulator credible, the authors should: (1) use a set of biophysical equations, with multi-compartmental modeling of currents and return currents; (2) use noised data from extracellular recordings; or (3) some combination thereof.

(2) The simulated dataset has to be extended in time. Maybe I missed something, but 500 units over 10 minutes, with some units having firing rates as low as 0.1 spikes/s, corresponds to some of the units firing an expected 60 spikes. This is clearly too short, and does not replicate the standard situation in extracellular experiments.

(3) The simulated dataset has to be extended in space. The choice of using NeuroPixels 1.0 geometry is a poor one. Many labs use other monolithic electrode arrays (MEAs, silicon probes, other rigid arrays); tetrodes remain a major tool, and flexible probes (polyimide, mesh) are evolving. Assessing algorithms over a single spatial architecture is likely to lead to local maxima in performance and potentially erroneous conclusions.

(4) The existing spike sorters evaluated are not completely described. Some sorters (e.g., SpyKING Circus and KS4) were described in previous publications, but it is unclear whether the implementation that was used for the present tests is exactly the same as those previously published. More importantly, some of the sorters evaluated (e.g., TDC, TDC2, SpyKING Circus 2) were never described in a peer-reviewed paper. This does not mean that they cannot be evaluated - but if they are, they must be described in full. Relying on the fact that the code is open source cannot replace a complete and accurate scientific description.

(5) Related to the above, all relevant code should be made available online in permanent repositories, not only in author-controlled ones.

(6) It is unclear why SpyKING Circus 2 and TDC2 are evaluated - these could potentially be described as straw men. I recommend reorganizing the manuscript so that after every module is evaluated separately based on a limited ground truth dataset, a single "best" sorter would be constructed, and then tested extensively (and compared to the de facto state of the art). Such reorganization would both demonstrate the utility of a modular approach and clarify the general usefulness of the outcome.

(7) The new algorithms developed, for example, clustering and template matching, have to be described in more detail, and demonstrated graphically on simple datasets. This can be done in supplementary material if the authors prefer not to extend the manuscript too much.

(8) This reviewer finds the description and interpretation of the results to be inadequate. As an example, focusing on Figure 5: The results in Figure 5A have to be supplemented and summarized as a scalar point estimate (e.g., median accuracy), an estimate of dispersion (e.g., using MAD, IQR, or SD), evaluated over multiple runs, and compared using statistical tests between tools and conditions (e.g., using a multi-dimensional analysis of variance, a mixed effect model, etc.). The results in Figure 5D must have an indication of dispersion. Any conclusions based on the numerical experiments must be based on these metrics and statistical evaluations.

(9) The entire MS would benefit from expert proofreading; there are many language errors, mostly in indefinite articles and grammatical numbers.

eLife Assessment

This valuable study presents a real-time system for identifying multiple unrestrained marmosets in a home cage setting using a combination of face detection and color-coded beads. However, there is incomplete evidence regarding the generalizability and robustness of the system to unconstrained multi-animal environments.

Reviewer #1 (Public review):

Summary:

The manuscript by Yang, Wang, and Cléry presents a lightweight pipeline for real-time identification of common marmosets in a laboratory setting. Models were trained and evaluated on data derived from a family of three closely related adults and a set of juvenile twins. Freely moving animals entered an enclosed space fixed to the housing cage door, which permitted the entry of individual animals for data acquisition. Utilizing YOLOv8-nano, identification was improved through the introduction of uniquely colored collar beads. Analyses of facial similarity showed close morphological relatedness amongst individuals and highlighted the need for highly discriminative classification. Overall, the authors offer a framework for identity tracking that prioritizes real-time inference. The authors demonstrate that combining facial detection with visual markers enables adequate identity assignment under controlled laboratory conditions with minimal cross-individual misclassification.

Strengths:

(1) The proposed pipeline offers a solution for real-time identity tracking in common marmosets. Its lightweight design enables deployment across a wide range of hardware configurations. Furthermore, if similar strategies are employed, this methodology is likely adaptable for other species with minimal modification.

(2) Evaluation of closely related individuals provides a necessary stress test for the discrimination of facial identity tracking.

Weaknesses:

(1) The pipeline's reliance on controlled animal isolation and small visual markers raises questions about the approach's generalizability to unconstrained multi-animal environments. The provided confusion matrices (Figures 6-8) indicate that the most common misclassifications are background-related, possibly suggesting that detection specificity is the primary source of error. All things considered, these findings raise concerns about performance in its use in socially dynamic and visually complex environments.

(2) The manuscript claims performance comparable to that of human experimenters but provides no explicit evidence to support these claims. While it is plausible that human experimenters may be less accurate in facial recognition tasks involving closely related marmosets, the authors don't provide evidence. Moreover, while that might be the case, the color-coded beads provide a salient identity cue for the model, which complicates the interpretation of this comparison grounded in facial recognition.

Reviewer #2 (Public review):

Summary:

In this study, Yang et al. develop a real-time system for automatic face detection and identification of multiple unrestrained common marmosets in a home cage setting.

Strengths:

The study aims to address an unmet need in behavioral neuroscience: the ability to non-invasively identify animals is crucial to the automated and rigorous study of neural behaviors; this is especially true for common marmosets, which are rapidly becoming a model system of choice for the study of complex social cognition. By using a YOLOv8 backbone, the study achieve human level performance, both in terms of precision and recall of the trained models.

Weaknesses:

The robustness of the system is not clear from the limited datasets presented. The use of color-coded beads undercuts the study's premise that the system achieves truly non-invasive tracking. Although the system achieves good performance in face detection, it does not perform as well for classification using faces alone (especially when the faces are similar, as in twin animals). Here, too, the color-coded beads play a key role in identity discrimination. The stated goals of the study and the actual results presented are therefore at odds.

Reviewer #3 (Public review):

Summary:

In this manuscript, Yang et al introduce a new method for automatically identifying marmosets in their home cage using a supervised deep learning method that recognizes the face and colored beads on marmoset collars. The authors show a high precision rate of identifying marmosets to levels comparable to a human experimenter. The method overall seems robust at identifying marmosets at different life stages and different settings; however, given the current form, I'm struggling to see the generalizability and experimental utility of this method.

Strengths:

(1) The authors provide a near-perfect automatic identification of marmosets in their home cage.

(2) This method is robust across lightning, camera angles, etc., making it potentially useful for marmoset (and other NHP) identification outside the housing cage as well

Weaknesses:

(1) Despite the almost perfect precision, in its current form, I'm failing to see how this method can be useful to other labs.

(2) This is a nice methods manuscript, but the authors do not present results to show how their method can be used outside of identifying marmosets inside their home cages in a small field of view.

(3) Reading the manuscript is strenuous, given its repetitive nature. Consolidating and shortening the results, as well as adding some definitions to the results section, would be helpful.

eLife Assessment

This useful study addresses the interesting question of how immune cells recognise infected erythrocytes in malaria. It proposes the parasite protein PfGBP-130 as an interaction partner of the human cell surface protein LFA 1, which could help explain how NK cells recognize infected erythrocytes. The conclusions are partially supported by pull-down and cell-based activation data. However, the overall evidence of direct interaction at the cell-cell interface and downstream effects is incomplete; stronger evidence is required to demonstrate surface exposure of PfGBP-130, as well as a direct role of this antigen in killing.

Reviewer #1 (Public review):

In this manuscript, the authors aim to determine the ligand on Plasmodium falciparum-infected erythrocytes for the NK cell integrin, LFA-1, following up on previous evidence that LFA-1 is important for immune cell-mediated recognition of iRBCs.

They start by incubating LFA-1 with iRBCs and show by flow analysis that a substantial population of these iRBCs binds to the LFA-1 (Figure 1C). They do conduct the control with uninfected RBCs, but put this in the supplementary material. As this is a critical control, I think that it should be moved to Figure 1C as it is essential to allow interpretation of the iRBC data. The authors also do not state which strain of P. falciparum they used (line 144). This is critical information as different strains have different variant surface antigens and should be included. With these changes, this data seems convincing.

They next incubated LFA-1 with the iRBCs, cross-linked and conducted a pulldown, identifying GP130 as a binding partner. Using cross-linkers is a dangerous strategy as it risks non-specific cross-linking. Did they try without cross-linking and find an interaction?

They raised antibodies to PfGBP and showed IFA, which reveals that these antibodies stain iRBCs (Figure 2Ciii). This experiment lacks a critical control of uninfected RBCs, which needs to be included to show that the staining is specific. Without this, it is not possible to conclude that there is iRBC-specific staining with PfGBP.

They then conduct a pulldown using LFA-Fc, which does show GP130 only in the presence of the LFA-Fc, but not when empty beads are used. This is convincing. BLI measurements are also used to study this interaction (Figure 2Ci). The BLI data is presented in such a way that any association phase is obscured by the y-axis, which makes it impossible to know whether there is binding here. I think that the data needs to be shown with some baseline before the addition of the ligand so that the association can be seen. The data is also a bit messy with a downward drift and the curves showing different shapes, for example, with the 1.0uM curve seeming to have a different association rate. Also, is this n=1? I think that this data needs to be repeated and replicated. As this is the only data which shows a direct interaction between LFA1 and GBP, as pulldowns are done with lysates, which might mean bridging components. I think that it is important to repeat the BLI or use additional biophysical methods to assess binding, to obtain more convincing data.

The authors next do some modelling of the putative complex. This is done by homology modelling and docking, which is not the most up-to-date method and is overinterpreted. Personally, I would remove this data as I did not find it convincing, and it is not important for the story. If the authors wish to include it, then I think that they should validate the modelling by mutagenesis to show that the residues which the models indicate might bind are involved in the interaction.

They next made GP130 and tested the binding of this to THP-1 cells, which are often used as a model for macrophages. They observe greater binding of PfGBP-Fc to these cells when compared with hIgG and show that LFA-1 siRNA reduces this binding. I was a little confused about how the flow plots related to the graph in the bottom right corner of Figure 3Bii. In the flow plots, hIgG control shows 12.8% of cells in the gated region, while the unstained cells has 5.63%, but the MFI data shows a decrease in binding for hIgG vs unstained cells. How is this consistent? Also, the siRNA reduces the number of cells in the gated region from 66.6% to 25.9%, which is still substantially more that 5.63% in the unstained control. This also doesn't seem quite consistent with the MFI data. Could the authors explain this? Also, perhaps an additional experiment would be to add soluble LFA-1 into this assay as an additional control to determine whether this blocks PfGBP binding to the THP-1 cells? It could be that there are additional mechanisms of binding which indicate why the siRNA has a partial effect. The same is true for the NK cell experiments in Figure 3Ci, in which the siRNA has a partial effect. The authors also test binding to HEK, HepG2 and 'stem' cells and claim 'only background levels of binding', but in each case, there is more binding to these cells by PfGBP-Fc than by hIgG, albeit less than in THP-1 and NK cells. Why have the authors decided that these increases are not significant? All in all, these experiments do indicate a role for the GBP-LFA1 interaction in the binding of immune cells to iRBCs, but perhaps not as absolutely as is suggested.

The authors next produce CHO cells with PfGBP on the surface. These cells bind to LFA-1 specifically. When these cells were incubated with primary NK cells, they did see increases in activation markers, which were reduced by the addition of anti-CD11a, suggesting these to be specific. They also conduct the same experiment with anti-GBP with iRBCs, but this is in a different figure. It would be easier for the reader if Figure 5B were in the same figure as Figure 4B, as it is related data using the same method. I found this data convincing, showing that the LFA1:GBP interaction does contribute to immune cell recognition and activation.

The authors next conduct an experiment in which they assess parasite growth in the presence of NK cells and in the presence of anti-GBP. They use Heochst staining as a measure of parasite growth and claim that NK cells reduce the number of parasites, but that anti-GBP abolishes this effect (Figure 5A). I found this experiment very unconvincing as there are small effects and no demonstration of significance. More commonly used approaches to study parasite growth are lactate dehydrogenase GIA assays or calcein-AM labelling. I did not find this experiment convincing and would either remove or supplement with additional data using a more robust assay, with repeats and tests of statistical significance.

In summary, the authors present a set of data which comes together to indicate an interaction between LFA1 and PfGBP on the Plasmodium-infected erythrocyte surface. Pulldown studies show convincingly that these two proteins co-precipitate, and BLI data suggest that this is direct. Also convincing is that NK cell activation can be reduced using antibodies against either LFA1 or PfGBP, indicating that this interaction does play a role in immune cell recognition of iRBCs.

Reviewer #2 (Public review):

Summary:

The authors used an LFA-1 αI-Fc fusion protein to pull down potential ligands and LC-MS/MS, leading to the selection of PfGBP-130 as a potential membrane protein on the surface of infected cells. PfGBP-130 antibodies were raised and used to support the surface localization. This putative ligand interacted strongly with LFA-1 (Kd = 15 nM). A presumed PfGBP-130 ectodomain interacts with monocytes and NK cells but not cells that lack LFA-1. PfGBP-130 antibodies also interfered with NK cell-mediated infected cell killing; the effect, although statistically significant, is modest. The authors propose that NK cells recognize infected cells via LFA-1 interaction with PfGBP-130 exposed on the host cell and that this interaction is critical to initiation of NK cell activation and killing of infected cells.

Major points:

(1) PfGBP-130 is proposed to be a membrane protein based on a single predicted transmembrane domain. Figures 2b and 3a show ribbon schematics with this TM domain at residues 51-68, in agreement with TM prediction algorithms such as TMHMM 2.0 and Phobius. However, this predicted TM is upstream of the PEXEL motif (residues 84-88, sequence RILAE), a conserved sequence for parasite protein export to host cytosol that is proteolytically processed at its 4th residue. Thus, residues 1-87 are removed from PfGBP-130 prior to export, yielding a mature protein without predicted TMs. Prior studies have determined that the mature PfGBP-130 lacks TMs and is retained as a soluble protein in host cell cytosol (PMID: 19055692, 35420481). Thus, the authors' model of PfGBP-130 as a surface-exposed membrane protein conflicts with both computational analysis of the mature protein and these prior reporter studies. An important simple experiment would be to evaluate PfGBP-130 membrane association in immunoblots using the authors' PfGBP-130 antibody after hypotonic lysis (PMID: 19055692) and after alkaline extraction (e.g. 100 mM NaCO3, pH 11 as frequently used, PMID: 33393463). If the prior studies and computational analyses are correct, the protein will be predominantly in the soluble and/or alkaline supernatant fractions.

(2) Many findings rely on the specificity of antibodies generated against PfGPB-130 or NK cell receptors. Although the authors have included key controls (use of isotype control antibodies, lack of anti-PfGBP-130 binding to uninfected cells), cross-reactivity between P. falciparum antigens is well-recognized and could significantly undermine the interpretation of experiments (PMID: 2654292 and 1730474 provide key examples of antigens recognized by antibodies raised against other proteins). For example, the surface localization in IFA experiments (Figure 2B(iii)) could reflect anti-PfGBP-130 binding to an unrelated parasite surface antigen, a possibility not addressed by any of the authors' controls. As another example, the iRBC lysate immunoblot using this antibody in Fig. 2B(iv) suggests a MW of 95 kDa, which corresponds to the unprocessed pre-protein before export; cleavage in the PEXEL motif yields a processed mature protein of 85 kDa, which should be readily resolved from the pre-protein in immunoblots (PMID: 19055692). A better immunoblot using immature infected cell stages might show both the pre-protein and the mature protein as a doublet band.

(3) PfGBP-130 is not essential for in vitro cultivation (PMID: 18614010 and MIS of 1.0 in the piggyBac mutagenesis screen as tabulated on plasmodb.org, indicating a highly dispensable gene). The authors should use the knockout line as a control in their IFA localization experiments to address antibody specificity. More fundamentally, their model predicts that NK cells should not recognize or kill infected cells from the knockout line when compared to their untransfected parent. Such results with the knockout line would compellingly support the authors' model without reliance on antibodies that may cross-react with other parasite antigens. PMID: 18614010 reported that the PfGBP-130 knockout exhibited increased membrane rigidity, suggesting an intracellular scaffolding protein rather than a surface localization and use as a ligand for LFA-1 interaction and NK cell-mediated killing.

(4) PfGBP-130 non-essentiality raises the question of why the gene would be retained if it triggers NK cell-mediated killing of infected cells in vivo. Presumably, this killing would pose strong selective pressure against retention of PfGBP-130. Some speculation is warranted to support the model.

Reviewer #3 (Public review):

Summary:

Malhotra and colleagues present evidence that the integrin LFA-1 on NK cells is a ligand for the Plasmodium falciparum protein GBP130 on the infected erythrocyte surface and that this interaction plays a role in the clearance of infected erythrocytes by NK cells.

The authors first select a subdomain contained within the CD11a subunit of LFA-1 as a probe to discover possible binding proteins on the infected erythrocyte surface. Parasite-infected erythrocytes stained positively with this probe; the level of staining increased as the parasites progressed through the life cycle. Using the LFA-1-based probe in cross-linking pull-down experiments, GBP130 was identified by mass spectrometry as a co-purifying parasite protein. The N-terminal portion of GBP130 was recombinantly expressed and shown to interact with LFA-1 alpha-I by biolayer interferometry experiments. The full-length extracellular domain of GBP130 was then recombinantly expressed and used to stain primary human NK cells and THP-1 cells. Knocking down LFA-1 by siRNA reduced staining by GBP130. To assess the contribution of GBP130 to the activation of NK cells, CHO cells exogenously expressing GBP130 were incubated with primary NK cells. Transfecting CHO cells with GBP130 led to increased activation of co-incubated NK cells compared to mock-transfected and compared to GBP130 transfected cells, with the inclusion of anti-CD11a to block NK cell adhesion. Finally, CHO cells expressing GBP130 led to increased activation of NK cells compared to mock-transfected CHO cells.

Overall, although the authors present data from NK cell killing assays that include appropriate controls, the data suggesting a direct interaction between PfGBP-130 and LFA-1 does not include the same necessary controls, for example, the use of blocking antibodies. Most critically, the biolayer interferometry experiments use a recombinant fragment of PfGBP-130, which does not include the residues predicted to be important for mediating specific interaction with LFA1. The biolayer interferometry data instead suggest non-specific interactions between PfGBP-130 and LFA1, as binding does not reach saturation.

eLife Assessment

This article presents valuable findings on how the timing of cooling affects the timing of autumn bud set in European beech saplings. The study leverages extensive experimental data and provides an interesting conceptual framework for the various ways in which warming can affect but set timing. The statistical analysis is compelling, but indicates some factors that may temper the authors' claims, while the designs of experiments offer incomplete support for the current claims as they rely on one population under extreme conditions for only one year each while a confounding effect (time in a chamber) sometimes lacks a control.

Reviewer #1 (Public review):

Summary:

This study provided key experimental evidence for the "Solstice-as-Phenology-Switch Hypothesis" through two temperature manipulation experiments.

Strengths:

The research is data-rich, particularly in exploring the effects of pre- and post-solstice cooling, as well as daytime versus nighttime cooling, on bud set timing, showcasing significant innovation. The article is well-written, logically clear, and is likely to attract a wide readership.

Comments on revisions:

This is the second round of review, and I am generally very satisfied with the authors' revisions. However, a few detailed issues still require attention:

The authors identified the summer solstice (June 21) as a phenological "switch point", but the flexibility of this switch point remains poorly understood. A more precise explanation of what "flexibility" means in this context is needed, along with a description of the specific experimental results that would demonstrate this flexibility.

The experiment did not directly measure the specific date of the phenological switch point. Instead, it was inferred by comparing temperature effects before and after the solstice. The manuscript should clearly state that this switch point remains an inferred conceptual node rather than a directly measured variable.

In Experiment 1, the effect of bud type (terminal vs. lateral) was inconsistent across the overall model and the different leafing groups. The authors should provide a more thorough discussion of potential reasons for this inconsistency. In addition, the statistical model for Experiment 1 indicates that the measured variables (summer cooling and leaf emergence date) explain only 23.4% of the variation in bud formation timing. This leaves over 76% of the variation unexplained, suggesting that other important factors are involved. The discussion should address this limitation in greater depth, moving beyond a focus on the measured variables.

Reviewer #2 (Public review):

In 'Developmental constraints mediate the summer solstice reversal of climate effects on European beech bud set [their original title]' Rebindaine and co-authors report on two experiments on Fagus sylvatica where they manipulated temperatures of saplings between day and night and at different times of year. I think the experiments are interesting, but I found the exact methods of them somewhat extreme compared to how the authors present them. Further, given that much of the experiment happened outside, I am not sure how much we can generalize from one year for each experiment, especially when conducted on one population of one species. I was also very concerned by the revisions.

I expand briefly on these concerns and a few others for readers of the paper (see `The below comments relate to my original review'). Subsequent edits to the paper addressed some of these by providing a new figure and moving around the methods. Further, I am at a loss about their hypothesis, when they write in their letter: "Importantly, the Solstice-as-Phenology-Switch hypothesis does not assume that the reversal is fixed to June 21." Why on earth reference the solstice if the authors do not mean to exactly reference the solstice?

The comments below relate to my original review with many of them still applying.

Methods: As I read the Results I was surprised the authors did not give more info on the methods here. For example, they refer to the 'effect of July cooling' but never say what the cooling was. Once I read the methods I feared they were burying this as the methods feel quite extreme given the framing of the paper. The paper is framed as explaining observational results of natural systems, but the treatments are not natural for any system in Europe of which I have worked in. For example a low of 2 deg C at night and 7 deg C during the day through end of May and then 7/13 deg C in July is extreme. I think these methods need to be clearly laid out for the reader so they can judge what to make of the experiment before they see the results.

I also think the control is confounded with growth chamber experience in Experiment 1. That is, the control plants never experience any time in a chamber, but all the treatments include significant time in a chamber. The authors mention how detrimental chamber time can be to saplings (indeed, they mention an aphid problem in experiment 2) so I think they need to be more upfront about this. The study is still very valuable, but -- again -- we may need to be more cautious in how much we infer from the results.

Also, I suggest the authors add a figure to explain their experiments as they are very hard to follow. Perhaps this could be added to Figure 1?

Finally, given how much the authors extrapolate to carbon and forests, I would have liked to see some metrics related to carbon assimilation, versus just information on timing.

Fagus sylvatica: Fagus sylvatica is an extremely important tree to European forests, but it also has outlier responses to photoperiod and other cues (and leafs out very late) so using just this species to then state 'our results likely are generalisable across temperate tree species' seems questionable at best.

Measuring end of season (EOS): It's well known that different parts of plants shut down at different times and each metric of end of season -- budset, end of radial expansion, leaf coloring etc. -- relate to different things. Thus I was surprised that the authors ignore all this complexity and seem to equate leaf coloring with budset (which can happen MONTHS before leaf coloring often) and with other metrics. The paper needs a much better connection to the physiology of end of season and a better explanation for the focus on budset. Relatedly, I was surprised the authors cite almost none of the literature on budset, which generally suggests is it is heavily controlled by photoperiod and population-level differences in photoperiod cues, meaning results may different with a different population of plants.

Somewhat minor comments:<br /> (1) How can a bud type -- which is apical or lateral -- be a random effect? The model needs to try to estimate a variance for each random effect so doing this for n=2 is quite odd to me. I think the authors should also report the results with bud type as fixed, or report the bud types separately.<br /> (2) I didn't fully see how the authors results support the Solstice as Switch hypothesis, since what timing mattered seemed to depend on the timing of treatment and was not clearly related to solstice. Could it be that these results suggest the Solstice as Switch hypothesis is actually not well supported (e.g., line 135) and instead suggest that the pattern of climate in the summer months affects end of season timing?

Author Response:

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

eLife Assessment

This article presents valuable findings on how the timing of cooling affects the timing of autumn bud set in European beech saplings. The study leverages extensive experimental data and provides an interesting conceptual framework of the various ways in which warming can affect bud set timing. The support for the findings is incomplete, though extra justifications of the experimental settings, clarifications of the interpretation of the results, and alternative statistical analyses can make the conclusions more robust.

We thank the editors and reviewers for their expert assessment of our findings and their interest in our conceptual framework. Below we respond to the specific reviewer and editor comments.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study provided key experimental evidence for the "Solstice-as-PhenologySwitch Hypothesis" through two temperature manipulation experiments.

Strengths:

The research is data-rich, particularly in exploring the effects of pre- and postsolstice cooling, as well as daytime versus nighttime cooling, on bud set timing, showcasing significant innovation. The article is well-written, logically clear, and is likely to attract a wide readership.

Thank you for your generous description of our study and the manuscript.

Weaknesses:

However, there are several issues that need to be addressed.

(1) In Experiment 1, significant differences were observed in the impact of cooling in July versus August. July cooling induced a delay in bud set dates that was 3.5 times greater in late-leafing trees compared to early-leafing ones, while August cooling induced comparable advances in bud set timing in both early- and late-leafing trees.

The study did not explain why the timing (July vs. August) resulted in different mechanisms. Can a link be established between phenology and photosynthetic product accumulation? Additionally, can the study differentiate between the direct warming effect and the developmental effect, and quantify their relative contributions?

We thank the reviewer for pointing out that we could improve our explanation of the different responses to July and August cooling in experiment 1. Whilst we incorporated this in the conceptual model and the figure caption (Fig. 1b), we now also address this topic in more depth in the discussion section, focussing on daylength and photosynthetic assimilation as the possible mediators of this change in responses (L350-371).

For the early-season development effect vs the late-season temperature effect we can use the leaf-out day-of-year (as a proxy for development), and the summer cooling treatments (direct temperature effect) to assess the relative importance of these two components of our model. We have now included a variance partitioning analysis following this logic, see L246-252 for methods, L278-281 for results.

(2) The two experimental setups differed in photoperiod: one used a 13-hour photoperiod at approximately 4,300 lux, while the other used an ambient day length of 16 hours with a light intensity of around 6,900 lux. What criteria were used to select these conditions, and do they accurately represent real-world scenarios? Furthermore, as shown in Figure S1, significant differences in soil moisture content existed between treatments - could this have influenced the conclusions?

This question may reflect a misunderstanding regarding the light availability that we hope to address with improved clarification. The duration and intensity of the lighting in these experiments was always set to reflect the average conditions experienced in Zurich for those respective times of the year. Day length in spring is shorter than it is in summer, so the durations were simply adjusted to reflect this reality. The 13-hour, 4,300 lux conditions in experiment 1 were only for the April-May period, when we reduced developmental rates for the late-leafing trees (L125-129). In July, the photoperiod was set to 16 hours and light intensity was approximately 7,300 lux (L150-154). This is equitable to experiment 2–when treatments were applied in June and July–where photoperiod was 16 hours and light intensity approximately 6,900 lux (L206-207). These conditions reflect the average daylengths in Zurich, and the maximum light intensity output by the chambers.

As mentioned in our initial author response, we do not think small differences in soil moisture levels should influence our conclusions. All pots were watered sufficiently to avoid water deficit, and all efforts were made to minimise differences in water availability. A Tukey honest significant difference test showed that only one treatment pair (6 - Late_July_Extreme vs. 7 - Early_August_Moderate, difference = 6%, p < 0.05) had significantly different soil water content, a pair whose responses are not compared. We have added words to this effect in the figure legend of Fig. S1.

(3) The authors investigated how changes in air temperature around the summer solstice affected primary growth cessation, but the summer solstice also marks an important transition in photoperiod. How can the influence of photoperiod be distinguished from the temperature effect in this context?

We agree that photoperiod likely plays a central role. Our conceptual model (Fig. 1) explicitly incorporates photoperiod as the framework within which temperature responses are regulated (L72-75, L627-629 & L638-641). The Solstice-as-Phenology-Switch hypothesis assumes that the annual progression of daylength sets the physiological “window” for trees’ responsiveness to temperature. Our experiments therefore focused on how temperature responses differ before versus after the solstice, while recognising that this reversal is likely enabled by the photoperiod signal. In other words, photoperiod provides the regulatory backdrop, and our results identify how diel and seasonal temperature cues are interpreted within that photoperiodic framework.

(4) The study utilized potted trees in a controlled environment, which limits the generalization of the results to natural forests. Wild trees are subject to additional variables, such as competition and precipitation. Moreover, climate differences between years (2022 vs. 2023) were not controlled. As such, the conclusions may be overgeneralized to "all temperate tree species", as the experiment only involved potted European beech seedlings. The discussion would benefit from addressing species-specific differences.

We agree that extrapolation from our experiments on Fagus sylvatica to other species and natural forests requires caution. However, it is precisely the controlled nature of our design that allowed us to isolate the precise mechanisms that appear to underpin the solstice switch, highlighting the role of diel and seasonal temperature variation. In natural systems, additional variables such as competition, precipitation, and soil heterogeneity can strongly influence phenology, but they also make it difficult to disentangle causal mechanisms. By minimising these confounding factors, our experiment provided a clear test of how temperature before and after the solstice regulates growth cessation.

To acknowledge the limitation, we have toned down statements about generalisation (e.g. “likely generalisable” to “other temperate tree species may display similarities”; L409-411) and explicitly call for follow-up studies across species and forest contexts (L413–414). At the same time, we highlight that our findings align with independent evidence from manipulative experiments, satellite observations, flux measurements, and ground-based phenology, which suggests the mechanisms we report may extend beyond the specific populations studied here.

Reviewer #2 (Public review):

In 'Developmental constraints mediate the summer solstice reversal of climate effects on European beech bud set', Rebindaine and co-authors report on two experiments on Fagus sylvatica where they manipulated temperatures of saplings between day and night and at different times of year. I enjoyed reading this paper and found it well written. I think the experiments are interesting, but I found the exact methods somewhat extreme compared to how the authors present them. Further, given that much of the experiment happened outside, I am not sure how much we can generalize from one year for each experiment, especially when conducted on one population of one species. I next expand briefly on these concerns and a few others.

Thank you for the kind comments. We appreciate your concerns regarding the severity of our treatments and the generalisability of our results, and you can find our detailed responses below.

Concerns:

(1) As I read the Results, I was surprised the authors did not give more information on the methods here. For example, they refer to the 'effect of July cooling' but never say what the cooling was. Once I read the methods, I feared they were burying this as the methods feel quite extreme given the framing of the paper. The paper is framed as explaining observational results of natural systems, but the treatments are not natural for any system in Europe that I have worked in. For example, a low of 2 {degree sign}C at night and 7 {degree sign}C during the day through the end of May and then 7/13 {degree sign}C in July is extreme. I think these methods need to be clearly laid out for the reader so they can judge what to make of the experiment before they see the results.

We understand the concern regarding the structure of the manuscript and note that the methods section was moved to the end of the paper in accordance with eLife’s recommended formatting. We have now moved the methods section before the results to ensure that readers are familiar with the treatments before encountering the outcomes.

We recognise that our temperature treatments were severe and do not mimic real world scenarios. They were deliberately designed to create large contrasts in developmental rates, thereby maximising our ability to detect the mechanisms underpinning the solstice switch. For example, the severe cooling between 4 April and 24 May was specifically designed to slow spring development as much as possible without damaging the plants (L129-L133). We have added text in the Methods to clarify this aim (L129-131 & L156-161).

Regarding presentation, treatment details are now described in both the Methods and the relevant figure legends. Given this structure, we have chosen not to restate the full treatment conditions in the main Results text to avoid repetition.

(2) I also think the control is confounded with the growth chamber experience in Experiment 1. That is, the control plants never experience any time in a chamber, but all the treatments include significant time in a chamber. The authors mention how detrimental chamber time can be to saplings (indeed, they mention an aphid problem in experiment 2), so I think they need to be more upfront about this. The study is still very valuable, but again, we may need to be more cautious in how much we infer from the results.

We appreciate the reviewer’s concern about the potential confounding effect of chamber exposure in experiment 1. We have now discussed this limitation more explicitly, adding further explanation to the Methods (L146-148) and Discussion (L345-346).

Note that chamber-related problems (e.g. aphid infestations) primarily occurred under warm chamber conditions, whereas our experiment 1 cooling treatments maintained low temperatures that suppressed such issues. This means that an equivalent “warm chamber control” could have been associated with its own artefacts, as trees kept under warm chamber conditions would have been exposed to additional stressors that were not present under natural growing conditions. To address this point, we included a chamber control in experiment 2. While aphid abundance was indeed higher in the warm chamber controls, chamber exposure itself had no detectable effect on autumn phenology. This suggests that the main findings of experiment 1 are unlikely to be artefacts of chamber conditions (L141145).

Nevertheless, we agree that chamber exposure remains a potential limitation of experiment 1, which requires clear acknowledgement. We now state this more explicitly in the manuscript while also emphasising that our results are supported by experiment 2 and by converging lines of external evidence.

(3) I suggest the authors add a figure to explain their experiments, as they are very hard to follow. Perhaps this could be added to Figure 1?

We have now added figures to the methods section to depict the experimental timelines and settings more clearly (Figs. 2 and 3).

(4) Given how much the authors extrapolate to carbon and forests, I would have liked to see some metrics related to carbon assimilation, versus just information on timing.

We agree that including more data on photosynthetic assimilation would be valuable for interpreting phenological responses. Indeed, it was our intention to collect this information. However, unfortunately, we experienced technical challenges with the equipment available to us during the experimental period, which prevented us from collecting a full dataset. Nevertheless, we were able to obtain measurements during pre-solstice cooling (now presented as Fig. S12, including data for all treatments), which show that cooling treatments strongly reduced assimilation rates compared to controls. Importantly, these strong reductions occurred across all cooling treatments, yet their phenological outcomes differed markedly, demonstrating that assimilation alone cannot explain the observed responses. As we discuss, our findings are consistent with previous manipulative and observational studies reporting a weak role of late-season assimilation in controlling autumn phenology.

(5) Fagus sylvatica is an extremely important tree to European forests, but it also has outlier responses to photoperiod and other cues (and leafs out very late), so using just this species to then state 'our results likely are generalisable across temperate tree species' seems questionable at best.

We agree that Fagus sylvatica has a stronger photoperiod dependence than many other European tree species. As we note in our response to Reviewer 1 (comment 4), our findings align with previous research across temperate northern forests. Within our framework, interspecific variation in leaf-out timing would not alter the overall response pattern, though it could shift the specific timing of effect reversals. For example, earlier-leafing species may approach completion of development sooner and thus show sensitivity to late-season cooling earlier than F. sylvatica. Nevertheless, we acknowledge the importance of not overstating generality. We have therefore revised the manuscript to phrase conclusions more cautiously (L409411) and highlight the need for further research across species (L413–414).

(6) Another concern relates to measuring the end of season (EOS). It is well known that different parts of plants shut down at different times, and each metric of end of season - budset, end of radial expansion, leaf coloring, etc - relates to different things. Thus, I was surprised that the authors ignore all this complexity and seem to equate leaf coloring with budset (which can happen MONTHS before leaf coloring often) and with other metrics. The paper needs a much better connection to the physiology of end of season and a better explanation for the focus on budset. Relatedly, I was surprised that the authors cite almost none of the literature on budset, which generally suggests it is heavily controlled by photoperiod and population-level differences in photoperiod cues, meaning results may be different with a different population of plants.

We thank the reviewer for pointing out that our discussion of the responses of different EOS metrics needs more clarity. We agree with much of this perspective, and we have added an additional analysis of leaf chlorophyll content data to use leaf discolouration as an alternative EOS marker (L179-195 for methods, L296-311 for results). On this we would like to make two important points:

Firstly, we agree that bud set often occurs before leaf discolouration, although this can depend on which definition of leaf discolouration is used. In experiment 1, bud set occurred on average on day-of-year (DOY) 262 and leaf senescence (50% loss of leaf chlorophyll) occurred on DOY 320. However, we do not necessarily agree that this excludes the combined discussion of bud set and leaf senescence timing. Whilst environmental drivers can affect parts of plants differently, often responses from different end-of-season indicators (e.g. bud set and loss of leaf chlorophyll) are similar, even if only directionally. Figure S11 shows how, across both experiments, treatment effects were tightly conserved (R² = 0.49) amongst the two phenometrics. In accordance with these revisions, we have updated the manuscript title to “Developmental constraints mediate the summer solstice reversal of climate effects on the autumn phenology of European beech” (L1-2).

Secondly, shifts in bud set timing remain the primary focus of the manuscript as these shifts are of direct physiological relevance to plant development and dormancy induction, whereas leaf discolouration may simply follow bud set as a symptom of developmental completion. This is supported by our results, which show stronger responses of bud set than leaf senescence (Figs. 4 & 5 vs. Figs. S9 & S10).

Following the reviewer’s suggestion, we have included more references on the topic of bud set and its environmental controls. The reviewer rightly stresses that photoperiod is considered the most important factor. As mentioned above (see Reviewer 1 comment 3), photoperiod is therefore key in our conceptual model. However, the responses we observed in F. sylvatica cannot be explained by photoperiod alone. For example, in experiment 1, July cooling delayed the autumn phenology of late-leafing trees but had negligible impact on early-leafing trees, even though both experienced the exact same photoperiod. Moreover, in experiment 2, day, night and full-day cooling showed substantial variations in their effects despite equal photoperiod across the climate regimes. This is why we suggest that the annual progression of photoperiod modulates the responses to temperature variations instead of eliciting complete control.

(7) I didn't fully see how the authors' results support the Solstice as Switch hypothesis, since what timing mattered seemed to depend on the timing of treatment and was not clearly related to the solstice. Could it be that these results suggest the Solstice as Switch hypothesis is actually not well supported (e.g., line 135) and instead suggest that the pattern of climate in the summer months affects end-of season timing?

We interpret this concern as relating to the flexibility in reversal timing that we observed. Importantly, the Solstice-as-Phenology-Switch hypothesis does not assume that the reversal is fixed to June 21. Rather the hypothesis implies that reversal occurs around the solstice, when photoperiod cues cause tree individuals to shift from accelerating to decelerating their seasonal development. Our conceptual model (Fig. 1) explicitly incorporates this flexibility by showing how the timing of the reversal depends on developmental speed: Individuals that develop more slowly (or leaf out later) cross the compensatory point later in the summer, whereas fast developing individuals reach it earlier.

Our experiments support this framework: pre-solstice full-day cooling delayed bud set, whereas post-solstice full-day cooling advanced it, with differences between early- and late-developing individuals consistent with the model. Moreover, the contrasting impacts of daytime vs. night time cooling demonstrate how diel conditions can further shape when the reversal is expressed. Thus, rather than contradicting the Solstice-as-Phenology-Switch hypothesis, our findings reinforce it and extend it by showing how flexibility arises from interactions between developmental progression, diel temperature responses, and photoperiod.

We have added an additional section in the Discussion that elaborates on how our results support the Solstice-as-Phenology-Switch hypothesis (L416-432).

Recommendations for the authors:

Reviewing Editor (Recommendations for the authors):

(1) The current strength of evidence is incomplete. Extra justifications of the experimental settings, clarifications of the interpretation of the results, and alternative statistical analyses could make the conclusions more solid.

We agree with the vast majority of the reviewer comments and have made the relevant edits. We believe that these have dramatically improved the clarity of the manuscript. The revised analyses have not changed our conclusions, though we have toned down generalisations.

(2) The Solstice as Switch hypothesis is about the effect of temperature warming. However, the two experiments did not simulate warming but rather cooling. Although a temperature difference can be obtained compared to the control in both cases, the impacts on plant physiology and phenology should still be different between the two scenarios.

Thank you for raising this point, which requires clearer communication in our manuscript. The Solstice-as-Phenology-Switch hypothesis posits that changes in temperature before and after the summer solstice have opposite effects on the autumn phenology of northern forest trees. While the hypothesis has most often been framed in terms of warming, the underlying mechanism concerns whether development is accelerated or slowed relative to ambient conditions. In essence, we are exploring the effect of changes in temperature – not warming per se. In warmer springs, development begins earlier and/or proceeds faster, while in colder springs the opposite occurs; the same logic applies to post-solstice conditions. We have extended our explanation in the Introduction (L69-71).

In our experiments, we applied cooling to create strong contrasts in developmental rates without damaging the trees. These treatments allow us to test the direction of phenological responses relative to ambient conditions. Thus, although we used cooling rather than warming, the results are directly informative for the Solstice-as Switch framework, which concerns the relative effect of temperature changes rather than the absolute direction of manipulation.

(3) The number of groups for bud type and summer temperature treatment is too small to be used as a random effect; it would be more appropriate to treat them as fixed-effect terms.

We have revised the analysis to include bud type as a fixed effect. There are only very minor numerical adjustments (e.g. rounding to 4.8 days instead of 4.9, see L271) and inferences are not altered. We also report the bud type effects for experiment 1 (L262-266) and experiment 2 (L292-293)

(4) Please add more clarifications for Figure 4 about what this figure is for and how you derived this figure, whether the data were from your experiments or others.

We have rewritten the caption for Figure 6 (Fig. 4 in the previous manuscript) to clarify where the data came from and how the figure was generated (L687-693). This figure serves as a visual guide to aid the understanding of the processes that may govern the patterns we have observed. Figure 6a uses data from previous studies on diel patterns in F. sylvatica, specifically growth (Zweifel et al., 2021) and photosynthetic assimilation rates (Urban et al., 2014). To aid visualisation, we linearly interpolated between measurements points, converted the values to a relative percentage (compared to observed maximum), and then smoothed the resulting curves. Based on the evidence from experiment 2, we suggest there may be a temperature threshold below which overwintering responses (e.g. bud set) are induced in F. sylvatica. Figure 6b depicts a theoretical diel pattern of this potential threshold. In simple terms, the threshold must be lower at night because nights are typically colder than days.

Reviewer #2 (Recommendations for the authors):

(1) How can a bud type -- which is apical or lateral -- be a random effect? The model needs to try to estimate a variance for each random effect, so doing this for n=2 is quite odd to me. I think the authors should also report the results with bud type as fixed, or report the bud types separately.

See point (3) in reviewing editor’s recommendations for the authors.

(2) Could the authors move the methods earlier and remind readers of them in the results?

We have addressed this issue, please see detailed response under reviewer 2’s concerns.

Urban O, Klem K, Holišová P, Šigut L, Šprtová M, Teslová-Navrátilová P, Zitová M, Špunda V, Marek MV, Grace J. 2014. Impact of elevated CO2 concentration on dynamics of leaf photosynthesis in Fagus sylvatica is modulated by sky conditions. Environmental Pollution 185: 271–280.

Zweifel R, Sterck F, Braun S, Buchmann N, Eugster W, Gessler A, Häni M, Peters RL, Walthert L, Wilhelm M, et al. 2021. Why trees grow at night. New Phytologist 231: 2174–2185.

eLife Assessment

The authors previously identified SLAP as a key suppressor of the Src tyrosine kinase and a tumor suppressor. In this important study, the authors show SLAP functions in a cell-autonomous fashion in colon stem cells and propose solid evidence that SLAP reduces tumorigenesis by inhibiting an EphB2-SRC axis.

Reviewer #1 (Public review):

Naim et al. use genetically engineered mouse models and tissue culture cell lines to investigate the role of the SLAP adaptor protein in colonic epithelium and colon tumour formation. The SLAP adaptor protein is known to be a negative regulator of tyrosine kinase signaling in hematopoietic cells, but its role outside the immune system is less well defined. Here, the authors use genetically engineered SLAP-deficient mice, tissue-specific SLAP KO, and colonic organoids to demonstrate that SLAP is expressed in cells of the colonic epithelium, where it acts as a cell-autonomous regulator of proliferation and differentiation. In addition, they provide biochemical evidence that loss of SLAP expression in cultured colonic organoids results in increased Src family kinase activity and global tyrosine phosphorylation, consistent with its known role as a suppressor of tyrosine kinase activity in immune cells. Consistently, treatment with an SRC kinase inhibitor inhibited the growth of SLAP-deficient organoids. These data provide solid evidence of a cell-autonomous role of SLAP in the colonic epithelium.

This work would be improved by further description and interpretation of the SLAP expression pattern shown in the constitutive and tissue-specific KO to further support the conclusions made. In Supplementary Figure 1, magnification of the colon epithelium areas with SLAP expression shown by b-gal and anti-SLAP staining, highlighting regions of interest, would better support the conclusions regarding SLAP expression in specific regions of the colon epithelium. In Supplementary Figure 1B, the authors should indicate that the SLAP staining referred to is epithelial and in resident immune cells, as is mentioned in the text. Also, magnification of the boxed area of LRG5 staining in Figure 1 would improve this figure.

Using a chemically induced model of colitis-associated cancer, the authors demonstrate that inactivation of SLAP shows a trend toward increased tumor formation (though this did not reach significance) as well as increased Src family kinase activity within tumors. Tumor spheres from SLAP-deficient animals showed enhanced growth that was suppressed by treatment with a Src family kinase inhibitor. Of note, the latter effect was specific to SLAP-deficient tumor spheres. These observations are convincing and support the authors' conclusion that SLAP has a tumor suppressor role in CRC through inhibition of SFK signaling.

Mechanistically, elevated expression of the RTK, EphB2, was detected in immunoblots of SLAP KO colonic crypts, while overexpression of SLAP in CRC cell lines downregulated EphB2 protein levels. Using an EPHB2 inhibitor, the role of EPHB2 in the growth of SLAP-deficient colonic organoids was demonstrated. While these data generally support the authors' conclusion that SLAP limits colonic organoid growth by downregulating RTKS such as EphB2 and downstream Src family kinase activity, they do not show which cell types/regions in the colonic epithelium have increased EPHB2 protein and how this relates to SLAP and phospho-SRC expression, as shown in Figure 1 and Figure S1 immunocytochemistry. The expression of EphB2 and its role in colonic tumorsphere growth were not investigated.

Overall, this work provides evidence of SLAP adaptor function in restricting tyrosine kinase signaling in the colonic epithelium, and suggests that loss of SLAP expression could promote tumorigenesis in this context.

Reviewer #2 (Public review):

Summary:

Protein tyrosine kinases are subject to diverse regulatory mechanisms controlling their activity in normal situations. The authors previously identified SLAP (Src-like adaptor protein), a negative regulator of receptor tyrosine kinase (RTK) signaling, as a key suppressor of the cytoplasmic tyrosine kinase SRC in the normal colon and demonstrated that SLAP is downregulated in a majority of colorectal cancers (CRCs).

In this study, the authors further explored SLAP functions in mouse models using constitutive and inducible epithelial-specific Slap deletion (villin-CreERT2 model). They found that loss of SLAP augments colonic epithelial cell proliferation and that induction of tumorigenesis by the AOM/DSS protocol mimicking CRC leads to more aggressive tumors in the absence of SLAP. This effect is apparently cell-autonomous as growth of normal and tumoral colonic organoids is SLAP-dependent in in vitro settings. Finally, the authors define that, in colon, SLAP represses EphB2, an RTK lying upstream of SRC, and show that inhibitors of EphB2 can partially limit tumorigenic development in vitro.

Strengths:

The manuscript is clearly and concisely written, making it easy to follow. The data obtained in the mouse models are very convincing.

Weaknesses:

Direct evidence that EphB2 is activated/phosphorylated in the absence of SLAP is lacking, as conclusions are only based on results obtained with inhibitors. Some other issues have to be addressed before acceptance, in particular, the relevance of the findings in CRC patients.

Author Response:

Public Reviews:

Reviewer #1 (Public review):

Naim et al. use genetically engineered mouse models and tissue culture cell lines to investigate the role of the SLAP adaptor protein in colonic epithelium and colon tumour formation. The SLAP adaptor protein is known to be a negative regulator of tyrosine kinase signaling in hematopoietic cells, but its role outside the immune system is less well defined. Here, the authors use genetically engineered SLAP-deficient mice, tissue-specific SLAP KO, and colonic organoids to demonstrate that SLAP is expressed in cells of the colonic epithelium, where it acts as a cell-autonomous regulator of proliferation and differentiation. In addition, they provide biochemical evidence that loss of SLAP expression in cultured colonic organoids results in increased Src family kinase activity and global tyrosine phosphorylation, consistent with its known role as a suppressor of tyrosine kinase activity in immune cells. Consistently, treatment with an SRC kinase inhibitor inhibited the growth of SLAP-deficient organoids. These data provide solid evidence of a cell-autonomous role of SLAP in the colonic epithelium.

This work would be improved by further description and interpretation of the SLAP expression pattern shown in the constitutive and tissue-specific KO to further support the conclusions made. In Supplementary Figure 1, magnification of the colon epithelium areas with SLAP expression shown by b-gal and anti-SLAP staining, highlighting regions of interest, would better support the conclusions regarding SLAP expression in specific regions of the colon epithelium. In Supplementary Figure 1B, the authors should indicate that the SLAP staining referred to is epithelial and in resident immune cells, as is mentioned in the text. Also, magnification of the boxed area of LRG5 staining in Figure 1 would improve this figure.

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

We agree that a more detailed description and visualization of SLAP expression in the colonic epithelium would strengthen our conclusions. In response, we will revise Fig 1 and S1 to better highlight SLAP expression patterns. Specifically, we will include higher-magnification images of the colonic epithelial regions in Suppl Fig 1, with clearly indicated regions of interest. We will also clarify in the legend of Suppl Figure 1B that SLAP staining is observed in both epithelial and resident immune cells, as described in the text. Additionally, we will provide a magnified view of the boxed area showing LGR5 staining in Figure 1 to improve clarity.

Using a chemically induced model of colitis-associated cancer, the authors demonstrate that inactivation of SLAP shows a trend toward increased tumor formation (though this did not reach significance) as well as increased Src family kinase activity within tumors. Tumor spheres from SLAP-deficient animals showed enhanced growth that was suppressed by treatment with a Src family kinase inhibitor. Of note, the latter effect was specific to SLAP-deficient tumor spheres. These observations are convincing and support the authors' conclusion that SLAP has a tumor suppressor role in CRC through inhibition of SFK signaling.

Mechanistically, elevated expression of the RTK, EphB2, was detected in immunoblots of SLAP KO colonic crypts, while overexpression of SLAP in CRC cell lines downregulated EphB2 protein levels. Using an EPHB2 inhibitor, the role of EPHB2 in the growth of SLAP-deficient colonic organoids was demonstrated. While these data generally support the authors' conclusion that SLAP limits colonic organoid growth by downregulating RTKS such as EphB2 and downstream Src family kinase activity, they do not show which cell types/regions in the colonic epithelium have increased EPHB2 protein and how this relates to SLAP and phospho-SRC expression, as shown in Figure 1 and Figure S1 immunocytochemistry. The expression of EphB2 and its role in colonic tumorsphere growth were not investigated.

Overall, this work provides evidence of SLAP adaptor function in restricting tyrosine kinase signaling in the colonic epithelium, and suggests that loss of SLAP expression could promote tumorigenesis in this context.

We also thank the reviewer for their positive comments regarding our tumor studies and the role of SLAP in regulating SFK signaling.

Regarding the mechanistic insights involving EphB2, we appreciate the reviewer’s suggestion to further define its spatial expression and relationship with SLAP and phospho-SRC. To address this, we plan to extend our analysis to assess the effect of Slap depletion on EphB2 protein levels throughout the intestinal epithelium.

We recognize that directly testing EphB2’s role in murine colonic tumorsphere formation would require a new cohort of SLAP knockout mice treated with AOM/DSS for 90 days, which is not feasible in the short term. To address this, we will instead use human colorectal cancer models to assess how SLAP modulation affects the response of tumoroids derived from cell lines to EphB2 inhibition, providing complementary mechanistic insights.

Overall, we believe these additions will strengthen the manuscript and more fully address the reviewer’s concerns.

Reviewer #2 (Public review):

Summary:

Protein tyrosine kinases are subject to diverse regulatory mechanisms controlling their activity in normal situations. The authors previously identified SLAP (Src-like adaptor protein), a negative regulator of receptor tyrosine kinase (RTK) signaling, as a key suppressor of the cytoplasmic tyrosine kinase SRC in the normal colon and demonstrated that SLAP is downregulated in a majority of colorectal cancers (CRCs).

In this study, the authors further explored SLAP functions in mouse models using constitutive and inducible epithelial-specific Slap deletion (villin-CreERT2 model). They found that loss of SLAP augments colonic epithelial cell proliferation and that induction of tumorigenesis by the AOM/DSS protocol mimicking CRC leads to more aggressive tumors in the absence of SLAP. This effect is apparently cell-autonomous as growth of normal and tumoral colonic organoids is SLAP-dependent in in vitro settings. Finally, the authors define that, in colon, SLAP represses EphB2, an RTK lying upstream of SRC, and show that inhibitors of EphB2 can partially limit tumorigenic development in vitro.

Strengths:

The manuscript is clearly and concisely written, making it easy to follow. The data obtained in the mouse models are very convincing.

Weaknesses:

Direct evidence that EphB2 is activated/phosphorylated in the absence of SLAP is lacking, as conclusions are only based on results obtained with inhibitors. Some other issues have to be addressed before acceptance, in particular, the relevance of the findings in CRC patients.

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

We agree that our conclusions regarding the SLAP–EphB2–SRC signaling axis rely in part on pharmacological inhibition. As outlined in the manuscript, EphB2 was selected primarily as a proof-of-concept receptor to illustrate how SLAP may indirectly regulate SRC activity through modulation of upstream receptor tyrosine kinases. We note that the use of two distinct classes of EphB inhibitors supports the robustness of our observations.

To further strengthen this aspect of the study, we will assess EphB2 phosphorylation status in SLAP-deficient conditions, which will provide more direct evidence of its activation state and its contribution to SRC signaling.

eLife Assessment

This study presents an important study of the relationship between morphogen signaling and cell fate choices in the forming zebrafish neural tube, addressing a topical question in developmental biology. The authors provide a solid characterization of the precision limit for gene regulatory networks interpreting Shh, with single-cell resolution and state-of-the-art in vivo approaches. While the depth of analysis is restricted, particularly by the number of cell traces, the study will be of interest to developmental biologists interested in cellular decision-making.

Reviewer #1 (Public Review):

[Editors' note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. Given the time elapsed since the original data collection, the authors have addressed the previous concerns by providing a more nuanced discussion of their results and acknowledging the limitations of the study to ensure the conclusions are supported by the existing data.]

Throughout the paper, the authors do a fantastic job of highlighting caveats in their approach, from image acquisition to analysis. Despite this, some conclusions and viewpoints portrayed in this study do not appear well-supported by the provided data. Furthermore, there are a few technical points regarding the analysis that should be addressed.

(1) Analysis of signaling traces

- Relevance of "modeled signaling level": It is not clear whether this added complexity and potential for error (below) provides benefits over a more simple analysis such as taking the derivative (shown in Figure 3C). Could the authors provide evidence for the benefits? For example, does the "maximal response" given a simpler metric correlate less well with cell fate than that calculated from the fitted response?

- Assumptions for "modeled signaling level": According to equation (1) Kaede levels are monotonically increasing. This is assumed given the stability of the fluorescent protein. However, this only holds for the "totally produced Kaede/fluorescence". Other metrics such as mean fluorescence can very well decrease over time due to growth and division. Does "intensity" mean total fluorescence? Visual inspection of the traces shown in Figure 2 suggests that "fluorescence intensity" can decrease. What does this mean for the inferred traces?

- Estimation of Kaede reporter half-live: It is not clear how the mRNA stability of Kaede is estimated. It sounds like it was just assessed visually, which seems not entirely appropriate given the quantitative aspects of the rest of the study. Also, given that Shh signaling was inhibited on the level of Smoothened, it is not obvious how the dynamics of signaling shutdown affect the estimate. Most results in Figure 7 seem to be quite robust to the estimate of the half-live. That they are, might suggest that the whole analysis is unnecessary in the first place. However, not all are. Thus, it would be important to make this estimate more quantitative.

(2) Assignment of fates and correlations

- Error estimate for cell-type assignment: Trying to correlate signaling traces to cell fate decisions requires accurate cell fate assignment post-tracking. The provided protocol suggests a rather manual, expert-directed process of making those decisions. Can the authors provide any error-bound on those decisions, for example comparing the results obtained by two experts or something comparable? I am particularly concerned about the results regarding the higher degree of variability in the correlation between signaling dynamics and cell fate in the posterior neural tube. Here, the expression of Olig2 does not seem to segregate between different assigned fates, while it does so nicely in the anterior neural tube. This would suggest to me that cells in the posterior neural tube might not yet be fully committed to a fate or that there could be a relatively high error rate in assigning fates. Thus, the results could emerge from technical errors or differences in pure timing. Could the authors please comment on these possibilities?

- Clustering and fates: One approach the authors use to analyze the correlation between signaling and fate is clustering of cell traces and comparison of the fate distributions in those clusters. There is a large number of clusters with only single traces, suggesting that the data (number of traces) might not be sufficient for this analysis. Furthermore, I am skeptical about clustering cells of different anterior-posterior identities together, given potential differences in the timing of signal reception and signaling. I am not convinced that this analysis reveals enough about how signaling maps to fate given the heterogeneity in traces in large clusters and the prevalence of extremely small clusters.

- Signaling vector and hand-picked metrics: As an alternative approach, that might be better suited for their data, the authors then pick three metrics (based on their model-predicted signaling dynamics) and show that the maximal response is a very good predictor of fate for different anterior-posterior identities. Previous information-theoretic analysis of signaling dynamics has found that a whole time-vector of signaling can carry much more information than individual metrics (Selimkhanov et al, 2014, PMID: 25504722). Have the authors tried to use approaches that make use of the whole trace (such as simple classifiers (Granados et al, 2018, PMID: 29784812), or can comment on why this is not feasible for their data? The authors should at least make clear that their results present a lower bound to how accurately cells can make cell-fate decisions based on signaling dynamics.

(3) Consequences of signaling heterogeneity

The authors focus heavily on portraying that signaling dynamics are highly variable, which seems visually true at first glance. However, there is no metric used or a description given of what this actually means. Mainly, the variability seems to relate to the correlation between signaling and fate. However, given the data and analysis, I would argue that the decoding of signaling dynamics into fate is surprisingly accurate. So signaling dynamics that seem quite noisy and variable by visual inspection can actually be very well discriminated by cells, which to me appears very exciting.

Indeed, simple features of signaling traces can predict cell fate as well as position (for anterior progenitors). Given that signaling should be a function of position, it naively seems as if signaling read-out could be almost perfect. It might be interesting to plot dorsal-ventral position vs the signaling metrics, to also investigate how Shh concentration/position maps to signaling dynamics, this would give an even more comprehensive view of signal transmission.

There remains the discrepancy between signaling traces and fate in the posterior neural tube. The authors point towards differences in tissue architecture and difficulties in interpreting a "small" Shh gradient. However, the data seems consistent with differences in timing of cell-fate decisions between anterior and posterior cells. The authors show that fate does initially not correlate well with position in the posterior neural tube. So, signaling dynamics should likely also not, as they should rather be a function of position, given they are downstream of the Shh gradient. As mentioned above, not even Olig2 expression does segregate the assigned fates well. All this points towards a difference in the time of fate assignment between the anterior and posterior. Given likely delays in reporter protein production and maturation, it can thus not be expected that signaling dynamics correlate better with cell fate than the reporter "83%". Can the authors please discuss this possibility in the paper?

Thus, while this paper represents an example of what the community needs to do to gain a better understanding of robust patterning under variability, the provided data is not always sufficient to make clear conclusions regarding the functional consequences of signaling dynamics.

Reviewer #2 (Public Review):

Summary:

In this work, Xiong and colleagues examine the relationship between the profile of the morphogen Shh and the resulting cell fate decisions in the zebrafish neural tube. For this, the authors combine high-resolution live imaging of an established Shh reporter with reporter lines for the different progenitor types arising in the forming neural tube. One of the key observations in this manuscript is that, while, on average, cells respond to differences in Shh activity to adopt distinct progenitor fates, at the single cell level there is strong heterogeneity between Shh response and fate choices. Further, the authors showed that this heterogeneity was particularly prominent for the pMN fate, with similar Shh response dynamics to those observed in neighboring LFP progenitors.

Strengths:

It is important to directly correlate Shh activity with the downstream TFs marking distinct progenitor types in vivo and with single cell resolution. This additional analysis is in line with previous observations from these authors, namely in Xiong, 2013. Further, the authors show that cells in different anterior-posterior positions within the neural tube show distinct levels of heterogeneity in their response to Shh, which is a very interesting observation and merits further investigation.

Weaknesses:

This is a convincing work, however, adding a few more analyses and clarifications would, in my view, strengthen the key finding of heterogeneity between Shh response and the resulting cell fate choices.

Author Response:

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

Public Reviews:

Reviewer #1 (Public Review):

Throughout the paper, the authors do a fantastic job of highlighting caveats in their approach, from image acquisition to analysis. Despite this, some conclusions and viewpoints portrayed in this study do not appear well-supported by the provided data. Furthermore, there are a few technical points regarding the analysis that should be addressed.

We thank the reviewer for the comments, due to the age of the work and logistic constraints, we are unable to perform further experiments and analysis to address some of the concerns. We revised conclusions and viewpoints accordingly to reflect reviewer concerns.

(1) Analysis of signaling traces

Relevance of "modeled signaling level": It is not clear whether this added complexity and potential for error (below) provides benefits over a more simple analysis such as taking the derivative (shown in Figure 3C). Could the authors provide evidence for the benefits? For example, does the "maximal response" given a simpler metric correlate less well with cell fate than that calculated from the fitted response?

We think the benefits of modeled signaling level are the conceptual accuracy to the extent possible with the data. It’s true that the assumptions brought-in may cause certain biases. We perform this and the simplest (raw data averaging, Fig.2). Intermediate results in between (such as the first derivative in Fig.3C) may correlate well or less well, but cannot be interpreted biologically.

Assumptions for "modeled signaling level": According to equation (1) Kaede levels are monotonically increasing. This is assumed given the stability of the fluorescent protein. However, this only holds for the "totally produced Kaede/fluorescence." Other metrics such as mean fluorescence can very well decrease over time due to growth and division. Does "intensity" mean total fluorescence? Visual inspection of the traces shown in Figure 2 suggests that "fluorescence intensity" can decrease. What does this mean for the inferred traces?

Yes the segmentations measure intensity in a fixed volume inside a cell, therefore it’s a spatial average (concentration) and is susceptible to cell volume changes. This has been noted in the revision. The raw measurement does fluctuate and can decrease, we think the short-time-scale fluctuations are likely measurement variations/errors rather than underlying big changes in concentration.

Estimation of Kaede reporter half-live: It is not clear how the mRNA stability of Kaede is estimated. It sounds like it was just assessed visually, which seems not entirely appropriate given the quantitative aspects of the rest of the study. Also, given that Shh signaling was inhibited on the level of Smoothened, it is not obvious how the dynamics of signaling shutdown affect the estimate. Most results in Figure 7 seem to be quite robust to the estimate of the half-live. That they are, might suggest that the whole analysis is unnecessary in the first place. However, not all are. Thus, it would be important to make this estimate more quantitative.

Yes we agree. Unfortunately we don’t have the quantitative data required to better estimate Kaede mRNA stability. The timing of Cyc inhibition to the ceasing of ptch mRNA production is roughly estimated but not necessarily precise in this context.

(2) Assignment of fates and correlations

Error estimate for cell-type assignment: Trying to correlate signaling traces to cell fate decisions requires accurate cell fate assignment post-tracking. The provided protocol suggests a rather manual, expert-directed process of making those decisions. Can the authors provide any error-bound on those decisions, for example comparing the results obtained by two experts or something comparable? I am particularly concerned about the results regarding the higher degree of variability in the correlation between signaling dynamics and cell fate in the posterior neural tube. Here, the expression of Olig2 does not seem to segregate between different assigned fates, while it does so nicely in the anterior neural tube. This would suggest to me that cells in the posterior neural tube might not yet be fully committed to a fate or that there could be a relatively high error rate in assigning fates. Thus, the results could emerge from technical errors or differences in pure timing. Could the authors please comment on these possibilities?

This is a very insightful point. We did examine the posterior data again (cross-checked by 2 co-authors) to make sure the mixed situation has correct cell fate assignment. As established by others’ and our previous studies (See also Fig.1A), the identification of MFPs and LFPs in zebrafish spinal cord is very robust. The MFPs are the apical constricted single column of cells along the midline on top of the notochord, and the LFPs are the 2 columns of cells next to MFP on both sides. LFPs’ expression of olig2:gfp did vary more in the posterior (timing of response/commitment could be a factor as the reviewer pointed out), but eventually the cells at those positions will be V3 interneurons or floor plates and have not been observed to make motoneurons. There are 3 low Olig2:GFP pMNs in the anterior dataset (Fig.2B’) and 3 high Olig2:GFP LFPs in the posterior dataset (Fig.2D’) that we checked carefully. The heterogeneity argument is based on the verified tracking and final positioning of these cells.

Clustering and fates: One approach the authors use to analyze the correlation between signaling and fate is clustering of cell traces and comparison of the fate distributions in those clusters. There is a large number of clusters with only single traces, suggesting that the data (number of traces) might not be sufficient for this analysis. Furthermore, I am skeptical about clustering cells of different anterior-posterior identities together, given potential differences in the timing of signal reception and signaling. I am not convinced that this analysis reveals enough about how signaling maps to fate given the heterogeneity in traces in large clusters and the prevalence of extremely small clusters.

We agree. Due to the age of the work and logistic constraints, we are unable to perform further experiments and analysis to enrich the tracks for this revision. We are aware of upcoming, independent studies with many more systematic tracks and analysis which will address these concerns. We have added the caveats the reviewer raised.

Signaling vector and hand-picked metrics: As an alternative approach, that might be better suited for their data, the authors then pick three metrics (based on their model-predicted signaling dynamics) and show that the maximal response is a very good predictor of fate for different anterior-posterior identities. Previous information-theoretic analysis of signaling dynamics has found that a whole time-vector of signaling can carry much more information than individual metrics (Selimkhanov et al, 2014, PMID: 25504722). Have the authors tried to use approaches that make use of the whole trace (such as simple classifiers (Granados et al, 2018, PMID: 29784812), or can comment on why this is not feasible for their data? The authors should at least make clear that their results present a lower bound to how accurately cells can make cell-fate decisions based on signaling dynamics.

Thanks for these suggestions. We are limited by the measurement noise, coverage window of the traces and the number of tracks to make use of the full dynamics in a more informative manner.

(3) Consequences of signaling heterogeneity

The authors focus heavily on portraying that signaling dynamics are highly variable, which seems visually true at first glance. However, there is no metric used or a description given of what this actually means. Mainly, the variability seems to relate to the correlation between signaling and fate. However, given the data and analysis, I would argue that the decoding of signaling dynamics into fate is surprisingly accurate. So signaling dynamics that seem quite noisy and variable by visual inspection can actually be very well discriminated by cells, which to me appears very exciting.

Yes – we agree that most cells are actually accurate in such a highly dynamic tissue. In the literature, the view has been more focused on how the GRN enables this accuracy. We therefore highlighted the heterogeneity and limit of accuracy of the GRN here. We added this point to make our presentation more balanced.

Indeed, simple features of signaling traces can predict cell fate as well as position (for anterior progenitors). Given that signaling should be a function of position, it naively seems as if signaling read-out could be almost perfect. It might be interesting to plot dorsal-ventral position vs the signaling metrics, to also investigate how Shh concentration/position maps to signaling dynamics, this would give an even more comprehensive view of signal transmission.

We’d refer readers to our earlier study Xiong et al., 2013 where ptch2:kaede, nkx2:gfp and olig2:gfp were plotted against position over time in single cell tracks. It was found that position was not a good predictor of signaling levels or cell fates at early stages when the cell fates were specified.

There remains the discrepancy between signaling traces and fate in the posterior neural tube. The authors point towards differences in tissue architecture and difficulties in interpreting a "small" Shh gradient. However, the data seems consistent with differences in timing of cell-fate decisions between anterior and posterior cells. The authors show that fate does initially not correlate well with position in the posterior neural tube. So, signaling dynamics should likely also not, as they should rather be a function of position, given they are downstream of the Shh gradient. As mentioned above, not even Olig2 expression does segregate the assigned fates well. All this points towards a difference in the time of fate assignment between the anterior and posterior. Given likely delays in reporter protein production and maturation, it can thus not be expected that signaling dynamics correlate better with cell fate than the reporter "83%". Can the authors please discuss this possibility in the paper?

Yes this is an important point/caveat of live signaling and fate tracking. As discussed in the manuscript, due to the sensitivity limit of fluorescent imaging, it’s difficult to determine the time when cells start to respond to the signal, and how variable that is from cell to cell. The posterior cells may be more variable in either spatial or temporal responses compared to the anterior and we are not able to distinguish that. However, signaling dynamics is not necessarily a good function of position or time either, there is no evidence for that in our results here. The 83% correlation is thus striking for the posterior progenitors indicating a certain robust logic in the GRN to capture a strong (even short-lived) response to Shh, regardless of position or time. This is an interest possibility (we do not claim it a mechanism as we have not tested it with perturbations) that challenges the prevailing view in the field that these progenitors integrate Shh exposure over time, or that they acquire positional information by reading a gradient.

The discussion has been modified to be more nuanced about these points.

Thus, while this paper represents an example of what the community needs to do to gain a better understanding of robust patterning under variability, the provided data is not always sufficient to make clear conclusions regarding the functional consequences of signaling dynamics.

We quite agree. Together with the reviewer, we look forward to seeing the publication of some recent, independent progresses overcoming the challenges in our work by other colleagues.

Reviewer #2 (Public Review):

Summary:

In this work, Xiong and colleagues examine the relationship between the profile of the morphogen Shh and the resulting cell fate decisions in the zebrafish neural tube. For this, the authors combine high-resolution live imaging of an established Shh reporter with reporter lines for the different progenitor types arising in the forming neural tube. One of the key observations in this manuscript is that, while, on average, cells respond to differences in Shh activity to adopt distinct progenitor fates, at the single cell level there is strong heterogeneity between Shh response and fate choices. Further, the authors showed that this heterogeneity was particularly prominent for the pMN fate, with similar Shh response dynamics to those observed in neighboring LFP progenitors.

Strengths:

It is important to directly correlate Shh activity with the downstream TFs marking distinct progenitor types in vivo and with single cell resolution. This additional analysis is in line with previous observations from these authors, namely in Xiong, 2013. Further, the authors show that cells in different anterior-posterior positions within the neural tube show distinct levels of heterogeneity in their response to Shh, which is a very interesting observation and merits further investigation.

Weaknesses:

This is a convincing work, however, adding a few more analyses and clarifications would, in my view, strengthen the key finding of heterogeneity between Shh response and the resulting cell fate choices.

We thank the reviewer for the comments, due to the age of the work and logistic constraints, we are unable to perform further experiments and analysis to address some of the concerns. We revised conclusions and viewpoints accordingly to reflect reviewer concerns.

Recommendations for the authors:

Reviewer #1 (Recommendations for The Authors):

Minor comments:

y-axis label suddenly changes to Ptch2-reporter level in Figure 5. Is what is plotted different from what is seen as examples in Figure 3?

Thanks! Figure 5 tracks are as Figure 3B, this has been annotated in the figure legends.

There are random bounding boxes in some of the figures.

Sometimes the m in "More dorsal" is stylized with a capital M and sometimes not. It is somewhat confusing as a name for cell types but it is fine if no alternative can be found.

This study unfortunately does not include markers that distinguish the interneurons dorsal to pMNs. We categorized them collectively as “more dorsal”.

Response-time is defined as "the amount of time with an above-basal Shh response". This seems to me as the definition of response duration. I would assume that response-time, means the time it takes until a response is first observed. Please consider changing this.

We did not use “duration” because a response time course recorded in these tracks may include multiple durations (on and off). The duration of exposure/response has been specifically used in the field as a single period of response. So it’s a sum of active responding time here. Clarified in the text.

Reviewer #2 (Recommendations for The Authors):

(1) The authors address several possible setbacks of transforming the measured fluorescence intensity of the patched reporter into a readout of the Shh signaling activity over time, however, one aspect that isn't directly addressed is the potential effect of differences in the z position of analyzed cells. These could, at least in principle, be sufficient to introduce significant noise in the fluorescence measurements. Can the authors subset their datasets by initial, as well as average, z position and then re-examine the measured trends for both Shh activity and the intensity of the cell fate reporters used in the study?

The zebrafish early neural plate/tube has a small thickness in z in dorsal-ventral imaging and the tissue is transparent. The depth-associated scattering contributes very little, if at all to the fluorescent signals in the imaged time window. This can be seen in the nuclear/membrane signal of the movies, which is largely uniform across the tissue in z in the neural tissue. It can also be seen that the notochord cells, further ventral, appears to be dimmer.

(2) It is critical for the validity of this study that the intensity of the patched reporter introduced by the authors in 2012, and used again in this study, faithfully represents the signaling activity of Shh. In this study, the authors provide measurements of the transcriptional rate of Kaede and additional modeling for this purpose. However, an important point is to determine how sensitive is the reporter to changes in Shh signaling of different magnitudes?

We consider this BAC reporter line a good (probably still the best live reporter) one as it resolves the endogenous gradient up to the dorsal interneuron domains (Huang et al., 2012, Xiong et al., 2013) and responds well to perturbations (Notch, Cyclopamine, etc). But it’s true that we don’t have information of how sensitive it responds to changes of different magnitude. As far as we know, there is no in vivo, single cell information of how Shh targets respond to signaling of different magnitudes.

(3) To strengthen the previous point, it would be nice to extend the analysis in Figure 2, at least partially, using other readouts for Shh activity (e.g. GBS-GFP)?

We have used a GBS-RFP line previously and found it to be lower resolution in terms of showing the DV gradient, compared to ptch2:kaede.

(4) It is unclear to me what is the relevant time window during which cells respond to Shh in the anterior versus posterior domains to determine progenitor specification. This is a concern to me, since: i) the average heterogeneity of Shh activity seems to increase strongly in time (Figure 2A/C); and ii) it is important to exclude that the finding of heterogeneous relationship between Shh activity and fate choices is largely driven by later timepoints, where potentially its activity is no longer relevant for cell fate specification. Can this point be clarified when this data is introduced in the manuscript and further discussed?

Yes this is an important point/caveat of live signaling and fate tracking. As discussed in the manuscript, due to the sensitivity limit of fluorescent imaging, it’s difficult to determine the time when cells start to respond to the signal, and how variable that is from cell to cell. The posterior cells may be more variable in either spatial or temporal responses compared to the anterior and we are not able to distinguish that.

(i) The ptch2:kaede reporter variability is higher in terms of magnitude (the signal gets brighter) in later times but the heterogeneity (overlap between difference cell fate groups) is lower in later times

(ii) Similarly, the heterogenous relationship is more pronounced in early time points. Since we do not know exactly when the activity becomes no longer relevant (from our earlier studies we do think that the cells become specified early, when Shh signaling is noisy), we modelled the response profile and searched for a good predictor. The maximum response stands out, particularly as a good indicator for the posterior cells, suggests an early window/time of specification.

Discussion has been modified to clarify these points.

(5) Is the response of the patched reporter, as well as cell fate reporters, to defined concentrations of exogenously provided Shh heterogeneous, for instance, in in vitro experiments?

Well-controlled (e.g., microfluidics and labeled Shh molecules) in vitro experiments will be fantastic future directions. Existing tissue explant + Shh dose approaches do not resolve the heterogeneity of exposure at single cell level but may be helpful in testing the limits and variabilities at different magnitudes.

(6) The source of noise in this system is not entirely clear to me. The authors seem to attribute the heterogeneity they observe to the way cells respond to Shh, but can it be excluded that the morphogen profile is itself noisy to start with? It is currently difficult to distinguish between these two possibilities, given that the Shh activity reporter used in this study is itself a transcriptional output of the pathway. Can the distribution of Shh itself be analyzed (even if in immunostainings) during neural tube formation?

Yes we fully agree. More quantitative analysis may help dissecting the sources of noise. The morphogen profile (particularly through time) will be great. Currently no reagent is available to achieve that. Studies using an engineered morphogen or tagged morphogen suggest that the pattern through tissue reasonably captures simple diffusion dynamics. However, at single cell level considerable randomness may still remain and difficult to quantitatively compare with still staining.

(7) It is unclear to me how the authors define the ultimate cell fate of cells in their analysis in Figure 6. The brief description in the methods and in the manuscript seems to suggest that, in combination with marker expression, the cell position is used as a criteria to assign the fate to the progenitors - if this is the case, I guess the observed relationship in Figure 6 with LMDV distance is almost a control? This could be clarified for the readers.

Yes indeed Figure 6 is a control as LMDV distances lead to final positions which form part of our determination of cell fates.

As established by others’ and our previous studies (See also Fig.1A), the identification of MFPs and LFPs in zebrafish spinal cord is very robust. The MFPs are the apical constricted single column of cells along the midline on top of the notochord, and the LFPs are the 2 columns of cells next to MFP on both sides. LFPs’ expression of olig2:gfp did vary more in the posterior (timing of response/commitment could be a factor as the reviewer pointed out), but eventually the cells at those positions will be V3 interneurons or floor plates and have not been observed to make motoneurons. There are 3 low Olig2:GFP pMNs in the anterior dataset (Fig.2B’) and 3 high Olig2:GFP LFPs in the posterior dataset (Fig.2D’) that we checked carefully.

The methods of fate determination are described in detail in methods.

(8) The graphs in Figures 6 and 7 are difficult to interpret. What proportion, and absolute number, of cells are "mis specified" when the authors show the distinct colored lines in the pMN, LFP or more dorsal domains? How do the authors determine where each cell fate domain begins and ends to access for "mis-specified" cells? Can the authors also provide the corresponding experimental images in the figure?

We apologize for the difficulties to interpret these figures. The graphs are a ranked list of all cells using the specified metric. The visual is to help generate an intuition of how mixed vs clear-cut the pattern is given the tested metric. They are not to be interpreted as the actual pattern in the tissue and there are no data images that show these patterns.

(9) Given the experimental limitations/technical challenges discussed by the authors during the paper, the score of around 90% of predictability of cell fate choices is rather high in the anterior domain, suggesting a minor functional role for heterogeneity in this region. Even for the posterior domain, the score of 83% predictability based on the maximum response to Shh is still relatively high. In my view, this author's conclusions should be adjusted to make this difference clearer in the abstract and discussion, highlighting that the heterogeneity between Shh response and cell fate choices, particularly in the pMN fate, are stronger in the posterior domain affecting the precision of cell fate decisions particularly in this region. Can the authors further comment on potential mechanisms driving this difference?

Yes – we agree that most cells are actually accurate in such a highly dynamic tissue. In the literature, the view has been more focused on how the GRN enables this accuracy. We therefore highlighted the heterogeneity and limit of accuracy of the GRN here.

We have added the fact that the Shh response is still the main determinant of the pattern despite the heterogeneity in the Discussion. We also further discussed possibilities of the anterior posterior differences.

(10) Following up from the previous point, the data in Figure 7 suggests that there might be different underlying mechanisms in how anterior and posterior cells interpret the Shh profile, with anterior cells potentially responding to the integrated concentration of Shh (since response time, average response, or maximum response to Shh all provide similar predictability scores for cell fate choices). In contrast, only the maximum response to Shh can provide a good prediction of posterior cell fate, consistent with a more instantaneous response to morphogen concentration (and thus potentially more error-prone measurement of the Shh profile?). This is a very interesting observation in my view. Could this be further tested?

Thank you. Yes we found this very interesting too. We discussed the possibilities, including the reviewer’s suggestion that these cells may have different contexts or strategy to interpret the signal. It is also possible that the anterior cells use the same strategy (maximum response at an early time) and the subsequent response/duration do not matter to their fate commitment. A precise approach to shut down Shh response dynamics in single cells (e.g., optogenetics) will enable the test of these ideas. We hope following up studies will take such approaches.

eLife Assessment

In this important study, DNA and RNA are co-imaged in single cells to show that the proximity of topologically associated domain (TAD) boundaries is uncoupled from the transcriptional activity of nearby genes. The evidence supporting these conclusions is convincing for the regions examined, with high-throughput imaging providing robust statistics. This work will be of interest to researchers studying genome architecture and its relationship to gene regulation.

Reviewer #2 (Public review):

Summary:

Almansour et al., investigate whether the proximity of TAD boundaries is directly linked to gene activity. The authors use high-throughput imaging to simultaneously measure the gene activity and physical distances between boundary regions in an allele-specific manner. Using transcriptional inhibitors, expression induction, and acute depletion of CTCF and cohesin, they test whether proximity of boundaries affects, or is affected by, gene activity.

Strengths:

The combined use of DNA and RNA imaging enabled simultaneous measurement of boundary proximity and transcriptional status at individual alleles. This allows single-allele correlation between boundary proximity and gene activity at multiple loci across thousands of alleles.

The use of both transcription inhibitors and transcription stimulation provides compelling and consistent evidence that boundary proximity can be disconnected from a gene's activity. The data convincingly support the conclusion that stable proximity between boundary regions is not required for ongoing transcription at the loci and timescales examined.

This work strengthens the emerging view that genome organization at the level of domain boundaries does not impose a deterministic control over transcription.

Strong disruption of boundary distances is only observed upon depletion of cohesin. Notably, this corresponds with the largest changes in gene activity. In contrast, depletion of CTCF actually had minimal impact on boundary distances and also had minimal impact on gene activity. This makes sense in light of previous work, where live cell imaging demonstrated that cohesin is more important for domain-structure, whereas CTCF is only important for blocking cohesin from continuing on, such that the fully formed loop occurs in a very small percentage of cells. Therefore, the fact that disruption of cohesin (more important for internal domain structure) affects gene activity while disruption of CTCF does not is exceptionally interesting.

Weaknesses:

In untreated cells, the distribution of distance measurements between boundary probes is exceptionally narrow. While depletion of RAD21 clearly demonstrates an ability to detect changes in this distribution, this tight baseline distribution may limit sensitivity to more subtle changes (like those one might expect from transcriptional influences).

This approach primarily tests the role of boundary interactions rather than domain organization as a whole.

Reviewer #3 (Public review):

Summary:

This study addresses a central question in genome organization: whether the positions of chromosomal domain boundaries are functionally coupled to gene activity. The authors use high-throughput imaging to simultaneously measure distances between boundary markers and nascent RNA production in thousands of individual cells, enabling direct comparison of boundary positions and transcriptional status at single chromosomal copies. This approach is applied across multiple loci, genes, and cell types, and is combined with acute transcriptional perturbations and depletion of architectural proteins to test the relationship between chromosome structure and gene activity in both directions.<br /> This work makes a meaningful contribution by providing direct, single-cell evidence that domain boundary positions and gene activity are largely uncoupled in this system.

Strengths:

A major strength of the work is its single-cell, single-allele resolution, which overcomes the averaging inherent to population-based assays. The authors consistently find that boundary proximity is largely independent of transcriptional status: active and inactive alleles have similar boundary distances, transcriptional perturbations do not shift boundary distributions, and depletion of the boundary factor CTCF does not alter gene expression, whereas cohesin depletion affects both boundary organization and transcription. These conclusions are supported by large numbers of alleles, multiple loci and cell types, and internal controls that distinguish boundary-specific effects from broader chromatin influences. The study offers a robust, scalable imaging pipeline that will be valuable for future studies linking genome organization and transcription at single-cell resolution.

Weaknesses:

The study has important limitations that are acknowledged by the authors. Measurements are restricted to distances between flanking boundaries and do not capture internal domain architecture, sub-domain structure, or finer-scale regulatory contacts. Resolution is limited by probe size and imaging, potentially masking subtle positional changes, and only a small set of loci is examined, leaving open how broadly the uncoupling generalizes. Some perturbation effects, particularly for RAD21, may involve mechanisms beyond boundary disruption.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) Conceptual framing and interpretation:

The central conclusion may require more precise framing to avoid potential overreach. The authors' interpretation equating "physical distance between TAD boundaries" with overall "TAD boundary architecture," and "transcriptional bursting events" with broader "gene activity," could benefit from clarification. This framing may not fully capture the temporal dynamics of transcription or the regulatory complexity within TADs. Furthermore, the broad conclusion of an uncoupled relationship appears to challenge extensive prior evidence from perturbation studies showing that disrupting TAD boundaries can alter gene expression. The authors' own observation of reduced gene activity upon RAD21 degradation suggests that global TAD disruption can affect transcription. A more precise and limited conclusion, acknowledging that their data demonstrate a lack of detectable correlation between boundary distance and bursting activity in their system, would be more accurate and help reconcile these findings with the existing literature.

We have modified statements throughout the manuscript, including in the title, to enhance the precision of our conclusions to avoid overreach. We have also added on p. 16 of our Discussion, a separate section on the limitations of the study, noting that our conclusions are limited to TAD boundary distances and do not reflect the structure of TAD boundaries or of TADs themselves. We have also expanded our Discussion of possible TAD functions on p. 14/15.

(2) Technical methods and data presentation:

(2.1) Accuracy and dimensionality of distance measurements: The manuscript does not clearly state whether distances are measured in 2D or 3D, nor does it sufficiently address precision limits. The stated Z-step size (1 µm) may be inadequate for accurately measuring sub-micron chromatin distances in 3D.

We state in both the Results and Methods that our data represent 2D distances derived from maximal-intensity projections of 3D image stacks. We previously published a detailed analysis of the precision of this measurement approach applied to chromatin interactions and documented the effect of 2D vs 3D analysis on these types of measurements. This study by Finn et al., 2022 is cited in the text. We also show in Figure S3 and mention on p. 6 and 10 that we observe similar results using either 2D or 3D analysis.

(2.2) Probe design and systematic error: The genomic coverage size of the BAC probes used for DNA FISH is not explicitly stated. Large probe coverage could inherently blur the precise spatial location of adjacent DNA loci. The reported average distance (~300 nm) may be influenced by the physical size of the probes, as well as systematic expansion or distortion introduced by sample fixation and FISH processing. Although such technical limitations are currently unavoidable, the authors should clarify how these factors might affect their ability to detect subtle distance changes.

The genomic location and size of all probes are provided in Supplementary Table 1. We deliberately use relatively large BAC probes both to generate robust, highly reproducible signals and to eliminate effects arising from local chromatin behavior. In line with earlier characterization of BAC probes (Finn et al., Cell, 2019; Finn et al., Methods, 2022), we find a strong correlation between micro-C/Hi_C interaction frequency and distance measurements. Systematic errors such as sample fixation and FISH processing have previously been evaluated by comparison to live cell data (see Finn et al., 2019) and found to be negligible, especially as all our analyses involve pairwise comparisons, which would both be similarly affected by systematic errors. We discuss resolution limits due to probe size in our new section on study limitations on p. 16.

(2.3) Data Visualization: The manuscript would benefit from including representative, zoomed-in regions of interest from the raw imaging data. This would allow readers to visually assess measured distance differences against background noise.

Raw images for inspection at any magnification are available at https://figshare.com/projects/_b_TAD_boundaries_and_gene_activity_are_uncoupled_b_/271078.

(2.4) Potential impact of resolution limits: In Figure 5, the micro-C data reveal a clear difference in interaction patterns inside versus outside the VARS2 locus TAD, yet the imaging data show no corresponding distance difference. This strongly suggests that the current imaging system, limited by optical resolution, probe size, and localisation accuracy, may be unable to resolve finer-scale spatial reorganizations associated with specific chromatin conformations (e.g., enhancer-promoter loops). The authors should explicitly discuss that their conclusion of "no coupling observed" may be constrained by the resolution and sensitivity of their method and does not preclude the possibility of detecting such associations with higher-precision measurements or in live-cell dynamics.

We generally see good agreement between micro-C/Hi-C data and distance measurements. Specifically, we consistently find closer proximity of boundaries than non-boundaries and larger boundary distances for larger TADs than for smaller ones, as presented throughout the study. Contrary to the reviewer’s statement, this is also true for the VARS2 TAD, where we find statistically significant shorter boundary distances for boundary probes (350 nm) vs the outside control region (390 nm), which correlates with the difference in micro-C interaction score of 5847 vs 2308. These data are shown in Figure 3. Regardless, we mention the issue of resolution due to probe size in the study limitation section on p. 16.

Reviewer #2 (Public review):

In untreated cells, the distribution of distance measurements between boundary probes is exceptionally narrow. While depletion of RAD21 clearly demonstrates an ability to detect changes in this distribution, this tight baseline distribution may limit sensitivity to more subtle changes (like those one might expect from transcriptional influences). In addition, the correlation analysis is asymmetric, primarily stratifying by transcriptional status and then comparing boundary distances. Given the central claim that boundary architecture does not influence gene activity, the analysis should be done from the opposite perspective (stratifying by boundary distance).

We mention the limitations on resolution of our approach in our discussion of study limitations on p. 16. An example of an analysis of stratifying by boundary distance is presented in Figure S3C. The conclusion is the same as stratifying by activity status.

Strong disruption of boundary distances is only observed upon depletion of cohesin. Notably, this corresponds with the largest changes in gene activity. In contrast, depletion of CTCF actually had minimal impact on boundary distances and also had minimal impact on gene activity. This makes sense in light of previous work, where live cell imaging demonstrated that cohesin is more important for domain-structure, whereas CTCF is only important for blocking cohesin from continuing on, such that the fully formed loop occurs in a very small percentage of cells. Therefore, the fact that disruption of cohesin (more important for internal domain structure) affects gene activity while disruption of CTCF does not is exceptionally interesting but is lacking from the discussion.

We mention the stronger effect of cohesion depletion compared to CTCF loss on gene expression in multiple locations in the Results and Discussion.

On a related note, this approach primarily tests the role of boundary interactions rather than domain organization as a whole, and it should be acknowledged that internal domain structures are not directly assessed.

We have modified statements throughout the manuscript to clearly indicate that our conclusions relate to boundary interactions rather than domain organization as a whole. We also discuss this in our section on study limitations.

The comparison to work in other organisms (particularly the comparisons made to Drosophila) should be handled with care. The mechanisms underlying domain formation differ substantially across these systems, particularly regarding the differences in CTCF's role.

We have modified our discussion of the data on Drosophila TADs, particularly as it relates to CTCF.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I couldn't locate the image data from figshare with the information provided (DOI: 10.6084/m9.figshare.30728354)

The link has been updated

https://figshare.com/projects/_b_TAD_boundaries_and_gene_activity_are_uncoupled_b_/271078.

Reviewer #2 (Recommendations for the authors):

Some of the conclusions overreach. I recommend revising the claims and discussion to focus solely on the proximity of boundaries, instead of TADs themselves. This would match better with your experiments.

We have modified statements throughout the manuscript, including in the title, to enhance the precision of our conclusions to avoid overreach. We have also added on p. 16, a separate section on limitations of our study, noting that our conclusions are limited to TAD boundary distances and do not reflect on the structure of the TADs themselves. We have also expanded our Discussion of possible TAD functions on p. 14/15.

I do disagree with the interpretation of the data in some parts, particularly at the end, where you state that disruption of TADs does not impact gene activity. For example, "Altogether, these results demonstrate that disruption of TAD boundary architecture is insufficient to alter gene expression" doesn't seem to match the results. Sure, depletion of CTCF minimally impacted gene expression, but it also minimally impacted the boundary distances. I think it is interesting that depletion of RAD21 had a bigger impact on both gene expression and boundary distances, and this should be discussed.

We have deleted this statement and now mention on p. 13 that RAD21 depletion affected gene expression, whereas loss of CTCF did not, and on p. 15 that loss of RAD21 had a greater impact on boundary distances than loss of CTCF. We have also expanded our Discussion of possible TAD functions on p. 14/15.

Related to this, I also recommend expanding the discussion of prior live-cell imaging work (ref 32) that showed that the fully formed CTCF loop is a rare event.

We have expanded the discussion of prior live-cell imaging work in several locations.

All the analysis is done from the perspective of the gene expression (e.g. group by expression and then measure distances). It would help to show that the inverse analysis is consistent (e.g. group by distances and measure gene expression).

Analysis of data stratified by distance measurements is shown in Figure S3C.

The discussion of the Drosophila work is strange, given that CTCF in Drosophila has a very different N-terminus, explaining why it doesn't really form loops. Sure, maybe it contributes to domains in some way, but probably no more than the dozens of other architectural proteins that have been found in that system. This work clearly focuses on CTCF-loop domains, so I would be specific about that. In the introduction, you do a good job of saying "in human cells, TADs are.... marked by binding sites for the CTCF protein". However, then you overgeneralize and state that TADs form via a process of loop extrusion. I think a simple statement before this to say that TADs in human cells have become somewhat synonymous with CTCF loop domains, and that is how you will use the term here. However, other organisms have TADs despite the lack of conservation of the CTCF protein.

We have modified the text accordingly.

On a related note, in the discussion, you cite two papers in Drosophila to state that "TADs form prior to the establishment of cell-type-specific gene expression programs", but that's not entirely accurate for those papers. They actually show that TADs occur coincident with ZGA, but loops form before that (ref 23: Espinola et al), or that there are indeed a few boundaries that show up before ZGA, but these correspond to RNA Polymerase (ref 24: Ing-Simmons et al.).

We have corrected this statement.

eLife Assessment

The manuscript presents important findings on how C. elegans can utilize distinct molecular mechanisms and circuit engagements to regulate tactile-dependent locomotory behaviours through the AFD thermosensory neuron. The authors use multiple techniques including microfluidics, genetic manipulations and single-copy rescue experiments, to provide compelling evidence for the role of AFD/AIB electrical synaptic connections in this behaviour. The reviewers are satisfied with the comprehensive revisions made by the authors.

Reviewer #1 (Public review):

Summary:

In this manuscript, Rosero and Bai examined how the well-known thermosensory neuron in C. elegans, AFD, regulates context-dependent locomotory behavior based on the tactile experience. Here they show that AFD uses discrete cGMP signalling molecules and independent of its dendritic sensory endings regulates this locomotory behavior. The authors also show here that AFD's connection to one of the hub interneurons, AIB, through gap junction/electrical synapses, is necessary and sufficient for the regulation of this context-dependent locomotion modulation.

Strengths:

This is an interesting paper showcasing how a sensory neuron in C. elegans can employ a distinct set of molecular strategies and different physical parts to regulate a completely distinct set of behaviors, which were not been shown to be regulated by AFD before. The experiments were well performed and the results are clear. However, there are some questions about the mechanism of this regulation. This reviewer thinks that the authors should address these concerns before the final published version of this manuscript.

Comments on revisions:

In this revised manuscript, Rosero and Bai satisfactorily addressed all the concerns raised by this reviewer regarding their original manuscript. This reviewer appreciates the authors' effort. This revised and improved manuscript demonstrates that a sensory neuron in C. elegans can utilize distinct molecular strategies and circuit engagements to regulate distinct sets of behaviors. This reviewer believes that the manuscript is suitable for final acceptance in eLife.

Reviewer #2 (Public review):

The goal of the study was to uncover the mechanisms mediating tactile-context-dependent locomotion modulation in C. elegans, which represents an interesting model of behavioral plasticity. Starting from a candidate genetic screen focusing on guanylate cyclase (GCY) mutants, the authors identified the AFD-specific gcy-18 gene as essential for tactile-context-dependent locomotion modulation. AFD has been primarily characterized as a thermosensory neuron. However, key thermosensory transduction genes and the sensory ending structure of AFD were shown here to be dispensable for tactile-context locomotion modulation. AFD actuates tactile-context locomotion modulation via the cell-autonomous actions of GCY-18 and the CNG-3 cyclic nucleotide-gated channel, and via AFD's connection with AIB interneurons through electrical synapses. At the circuit level, AIB also receive inputs from the mechanosensory neuron FLP, which was also shown to be relevant for tactile-context-dependent locomotion modulation.

For this study, the authors combined a very clever microfluidic-based behavioral assay with a large set of genetic manipulations to dissect the molecular and cellular pathways involved. Rescue experiments with single-copy transgenes are particularly convincing. The study is very clearly written, and the figures are nicely illustrated with diagrams that effectively convey the authors' interpretation. Overall, the convergence of behavioral assays, genetics, and circuit analysis provides convincing support for the proposed role of the AFD-AIB connection, potentially downstream of FLP via synapic and of other mechanosensory neurons via extra-synaptic communication.

The facts that AFD mediates tactile-context locomotion modulation, that this role relies on GCY-18, and on electrical synapses linking AFD to AIB are new, somewhat unexpected, and interesting. The study raises intriguing and addressable questions about the role of innexin-based cellular communication in a multimodal sensory-behavior microcircuit, including the direction and nature of the signal(s) transmitted through these electrical synapses. These questions remain difficult to address in most experimental systems. The compact and genetically tractable nervous system of C. elegans provides a powerful entry point for addressing them in the context of an intact in vivo circuit.

Reviewer #3 (Public review):

Summary:

Rosero and Bai report an unconventional role of AFD neurons in mediating tactile-dependent locomotion modulation, independent of their well-established thermosensory function. They partially elucidate the signaling mechanisms underlying this AFD-dependent behavioral modulation. The regulation does not require the sensory dendritic endings of AFD but rather the AFD neurons themselves. This process involves a distinct set of cGMP signaling proteins and CNG channel subunits separate from those involved in thermosensation or thermotaxis. Furthermore, the authors demonstrate that AIB interneurons connect AFD to mechanosensory circuits through electrical synapses. They conclude that, beyond its primary function in thermosensation, AFD contributes to context-dependent neuroplasticity and behavioral modulation via broader circuit connectivity.

While the discovery of multifunctionality in AFD is not entirely unexpected, given the limited number of neurons in C. elegans (302 in total), the molecular and cellular mechanisms underlying this AFD-dependent behavioral modulation, as revealed in this study, provide valuable insights into the field.

Strengths:

(1) The authors uncover a novel role of AFD neurons in mediating tactile-dependent locomotion modulation, distinct from their well-established thermosensory function, providing an important conceptual contribution to our understanding of how individual neurons can support multiple, mechanistically separable behavioral functions.

(2) They provide meaningful mechanistic insight into how AFD, GCY-18-dependent cGMP signaling, and AFD-AIB electrical coupling contribute to this AFD-dependent behavioral modulation.

(3) The neural behavior assays utilizing two types of microfluidic chambers (uniform and binary chambers) are innovative and well-designed. In the revised manuscript the authors introduce a removable-barrier assay that physically separates exploration and assay phases. This independent behavioral approach addresses prior concerns about ongoing sensory input and confirms that tactile experience alone is sufficient to modulate locomotion.

(4) By comparing AFD's role in locomotion modulation to its thermosensory function throughout the study, the authors present strong evidence supporting these as two independent functions of AFD.

(5) The finding that AFD contributes to context-dependent behavioral modulation is significant, further reinforcing the growing evidence that individual neurons can serve multiple functions through broader circuit connectivity.

Weaknesses:

While the requirement for AFD, GCY-18, and AFD-AIB electrical coupling is well supported, the directionality of information flow and the precise mode of interaction between mechanosensory neurons, AIB, and AFD remain unclear and an area of future studies.

Overall, the authors successfully achieve their primary aim of identifying and characterizing a novel role for AFD in tactile experience-dependent locomotion modulation. This work contributes meaningfully to the growing body of literature demonstrating multifunctionality and context-dependent reconfiguration of individual neurons within compact nervous systems.

Author Response:

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

Public Reviews:

Although the reviewers agree on the potential importance of this study, they have brought out multiple pertinent queries with respect to the interpretation of some of the results presented in the manuscript, that the authors should consider addressing. The reviewers have also suggested modifications that would increase the clarity of the manuscript.

We appreciate the thoughtful evaluation of our manuscript by the reviewers and the editor. We are encouraged by their recognition of the importance of our study and have carefully considered all the points raised. In response, we have added new data and revised the text to address the concerns and improve the clarity of the manuscript. Our detailed responses to the reviewers’ comments are provided below.

Reviewer #1 (Public review):

Summary:

In this manuscript, Rosero and Bai examined how the well-known thermosensory neuron in C. elegans, AFD, regulates context-dependent locomotory behavior based on the tactile experience. Here they show that AFD uses discrete cGMP signaling molecules and independent of its dendritic sensory endings regulates this locomotory behavior. The authors also show here that AFD's connection to one of the hub interneurons, AIB, through gap junction/electrical synapses, is necessary and sufficient for the regulation of this context-dependent locomotion modulation.

Strengths:

This is an interesting paper showcasing how a sensory neuron in C. elegans can employ a distinct set of molecular strategies and different physical parts to regulate a completely distinct set of behaviors, which were not been shown to be regulated by AFD before. The experiments were well performed and the results are clear. However, there are some questions about the mechanism of this regulation. This reviewer thinks that the authors should address these concerns before the final published version of this manuscript.

Weaknesses:

(1) The authors argued about the role of prior exposure to different physical contexts which might be responsible for the difference in their locomotory behavior. However, the worms in the binary chamber (with both non-uniformly sized and spaced pillars) experienced both sets of pillars for one hour prior to the assay and they were also free to move between two sets of environments during the assay. So, this is not completely a switch between two different types of tactile barriers (or not completely restricted to prior experience), but rather a difference between experiencing a more complex environment vs a simple uniform environment. They should rephrase their findings. To strictly argue about the prior experience, the authors need to somehow restrict the worms from entering the uniform assay zone during the 1hr training period.

We agree that, in the original design, worms in the binary chamber experience a more complex physical environment while retaining access to both exploration and assay zones. We have therefore revised the manuscript to more clearly distinguish between behavioral differences due to exposure to a complex environment and modulation driven by prior experience.

To directly test whether locomotion modulation can be sustained by prior physical experience in the absence of continued access to the exploration zone, we introduced a barrier-based assay that prevents worms from re-entering the exploration zone before locomotion is measured. The results section has been revised accordingly to explicitly address this point.

Revisions to the manuscript:

Lines 122-139: Added two paragraphs describing the new assay and summarizing the corresponding results.

“Because worms in the binary chamber are exposed to both pillar types and remain free to move between exploration and assay zones, the behavioral differences described above could reflect exposure to a more complex physical environment rather than prior experience alone. To directly test whether locomotion is modulated by prior physical experience independently of continued access to the exploration zone, we designed microfluidic chambers in which the assay zone could be separated from the exploration zone by a removable barrier (Fig. 1–Supplement 1A). In these chambers, worms were initially allowed to explore the entire device, including exploration zones that either matched or differed from the assay zone. A barrier was then inserted to prevent worms in the assay zone from re-entering the exploration zones.

Under these conditions, locomotion immediately after barrier insertion was higher in worms that had previously explored physical settings matching the assay zone (205 ± 8 µm/s) than in worms that had explored non-matching settings (151 ± 7 µm/s; p = 0.006; Fig. 1–Supplement 1B). This difference persisted when worms were recorded 40 minutes after barrier insertion, with animals in matching chamber retaining their higher locomotion rates (218 ± 11 µm/s) compared to those in non-matching chambers (185 ± 8 µm/s; p = 0.02; Fig. 1–Supplement 1B). These findings demonstrate that prior exploration of distinct physical environments can modulate locomotion even when worms are prevented from returning to those environments, supporting a role for prior physical experience independent of ongoing sensory input.”

Figure 1–Supplement 1: New figure showing the experimental design and behavioral results.

(2) The authors here argued that the sensory endings of AFD are not required for this novel role of AFD in context-dependent locomotion modulation. However, gcy-18 has been shown to be exclusively localized to the ciliated sensory endings of AFD and even misexpression of GCY-18 in other sensory neurons also leads to localizations in sensory endings (Nguyen et. al., 2014 and Takeishi et. al., 2016). They should check whether gcy-18 or tax-2 gets mislocalized in kcc-3 or tax-1 mutants.

As the reviewer suggested, we examined GCY-18 localization in wild type animals and in mutants with defective sensory microvilli using a split-GFP strategy (He et al., 2019). We generated a gcy18::gfp11×7 knock-in strain using CRISPR–Cas9 to visualize endogenous GCY-18 localization. Consistent with prior studies, GCY-18 localized strongly to the AFD dendritic ending in wild-type animals (Figure 4– Supplement 1A, A′, A′′), with an additional weaker signal detectable near the soma and axon (Figure 4– Supplement 1A′′′).

In kcc-3 mutants, GCY-18 remained localized to the distal dendrite despite disruption of sensory microvillar morphology (Figure 4–Supplement 1B–B′′). Similarly, in ttx-1 mutants, which completely lack AFD sensory microvilli, GCY-18 still localized to the distal dendrite (Figure 4–Supplement 1C–C′′) and remained detectable near the soma and axon (Figure 4–Supplement 1C′′′).

In the revised manuscript, we clarify both the implications and the limitations of these imaging experiments, noting that “although these experiments do not identify the precise subcellular site at which GCY-18 acts, they show that disruption of sensory microvilli does not substantially alter GCY-18 localization within AFD.” The exact site at which GCY-18 functions to support locomotion modulation therefore remains an important open question for future investigation.

Revisions to the manuscript:

Figure 4-Supplement 1: Added a new figure reporting GCY-18 localization in wild type and mutant worms.

Lines 268-280: Added a new paragraph reporting GCY-18 localization in wild type, kcc-3, and ttx-1 mutants and clarifying its relevance to the reviewer’s concern.

“Given that gcy-18 is required for context-dependent locomotion modulation and that GCY-18 localizes to the distal dendrite of AFD, we next examined how disruption of sensory microvilli affects its localization in AFD. We used a split-GFP strategy to visualize endogenous GCY-18 [73]. A tandem array of seven GFP11 β-strands (GFP11x7) was inserted at the C-terminus of GCY-18 using CRISPR-Cas9. When complemented with GFP1-10, GCY-18::GFP11x7 fluorescence was strongly enriched at the AFD sensory microvilli near the nose (Fig. 4–Supplement 1A-A′′), consistent with previous reports [42,74,75]. In addition, weaker but reproducible GCY-18 signal was detected near the AFD soma and axon (Fig. 4–Supplement 1A′′′). Importantly, in kcc-3, which exhibit disrupted sensory microvilli, and ttx-1 mutants, which lack sensory microvilli, GCY-18 remained localized to the distal dendrite and was still detectable near the soma and axon (Fig. 4–Supplement 1B-B′′’ and 1C-C′′′). Although these experiments do not identify the precise subcellular site at which GCY-18 acts, they show that disruption or loss of sensory microvilli does not substantially alter GCY-18 localization within AFD.”

(3) MEC-10 was shown to be required for physical space preference through its action in FLP and not the TRNs (PMID: 28349862). Since FLP is involved in harsh touch sensation while TRNs are involved in gentle touch sensation, which are the neuron types responsible for tactile sensation in the assay arena? Does mec-10 rescue in TRNs rescue the phenotype in the current paper?

We performed cell-specific rescue experiments of mec-10. Single-copy expression of mec-10 cDNA in either FLP neurons alone (egl-44p) or TRNs alone (mec-18p) did not restore context-dependent locomotion modulation (Fig. 5A). In contrast, co-expression in both FLP and TRNs (egl-44p::mec-10 + mec18p::mec-10), as well as expression from the mec-10 promoter, rescued the phenotype.

These results indicate that input from multiple mec-10-expressing neurons, including both FLP and TRNs, is required for context-dependent locomotion adjustment. This requirement differs from spatial preference behavior, where mec-10 acts specifically in FLP (Han et al., 2017), suggesting distinct mechanosensory circuits are engaged by different tactile-driven behaviors.

Revisions to the manuscript:

Fig. 5A: Updated to include the cell-specific rescue data.

Lines 317-331: Added a new paragraph describing these findings.

“The mec-10 gene is expressed in several mechanosensory neurons, including the six touch receptor neurons (TRNs) and the polymodal nociceptors FLP and PVD [77,79]. To determine which neurons are required for tactile-dependent locomotion modulation, we expressed mec-10 cDNA under cell-specific promoters: mec-18p (TRNs) [80], egl-44p (FLP) [81], or mec-10p (TRNs, FLP, and PVD) [79]. Expression in either FLP or TRNs alone did not restore modulation, as worms carrying egl-44p::mec-10 (Δspeed: -11± 4%) or mec-18p::mec-10 (Δspeed: -13 ± 4%) transgenes showed significantly reduced Δspeed compared to wild type (Δ speed: N2: 33 ± 6%; p < 0.0001 for both; Fig. 5A). By contrast, mec-10 co-expression in both FLP and TRNs (Δspeed: 16 ± 4%), or expression from the mec-10 promoter (Δspeed: 23 ± 4%), restored Δ speed to wild type levels (p = 0.20 and p = 0.57, respectively; Fig. 5A). These findings indicate that mec10 expression across multiple mechanosensory neuron types is required for context-dependent locomotion modulation. It is also worth noting that, while both tactile-dependent locomotion modulation and previously reported spatial preference require FLP, only the former depends on TRNs. Together, these findings suggest that distinct subsets of mechanosensory neurons differentially contribute to behaviors shaped by tactile experience.”

(4) The authors mention that the most direct link between TRNs and AFD is through AIB, but as far as I understand, there are no reports to suggest synapses between TRNs and AIB. However, FLP and AIB are connected through both chemical and electrical synapses, which would make more sense as per their mec10 data. (the authors mentioned about the FLP-AIB-AFD circuit in their discussion but talked about TRNs as the sensory modality). mec-10 rescue experiment in TRNs would clarify this ambiguity.

We agree with the reviewer that there are no reported synapses between TRNs and AIB, and we have revised Fig. 5 and the corresponding text to clarify this point. In the revised manuscript, we removed any implication of a direct TRN-AIB connection and instead focus on the established FLP-AIB-AFD pathway, while considering potential indirect contributions from TRNs.

As the reviewer suggested, we performed cell-specific mec-10 rescue experiments. Expression of mec-10 in either FLP alone or TRNs alone was insufficient to restore tactile-dependent locomotion modulation, whereas co-expression in both cell types rescued the phenotype (revised Fig. 5A). These results indicate that FLP is essential for this behavior, consistent with the known FLP-AIB-AFD connectivity, and that TRNs are also required.

Given that TRNs lack direct synapses with AIB, TRN requirement suggests the involvement of indirect communication, likely mediated through modulatory mechanisms such as neuropeptide signaling. Accordingly, we have revised the model (revised Fig. 5C) and the corresponding text to clarify that tactiledependent locomotion modulation integrates inputs from multiple mec-10-expressing neurons and does not rely on a direct TRN-AIB synaptic connection.

Revisions to the manuscript:

Lines 334–345: Revised paragraph to clarify circuit logic and remove implication of direct TRN-AIB synapses.

“Touch-sensitive neurons that express mec-10, including TRNs, FLP, and PVD, do not form direct synapses with AFD, suggesting that tactile information is relayed through intermediary neurons. Because the interneuron AIB receives synaptic input from FLP and forms electrical synapses with AFD, we hypothesized that AIB could serve as a conduit for mechanosensory signals to reach AFD. To test whether AIB is required for tactile-dependent modulation, we examined locomotion in worms with genetically ablated AIB neurons using npr-9p::caspase expression [82]. AIB-ablated worms failed to adjust locomotion speed, showing a near-complete loss of modulation (∆speed: -1 ± 5%) compared to wild type (30 ± 8%, p = 0.001, Fig. 5B). These results demonstrate that AIB is required for AFD-mediated tactile-dependent locomotion modulation. However, because mec-10-expressing TRNs are also required, additional pathways beyond AIB likely contribute to transmitting tactile information to AFD, potentially involving indirect synaptic connections through other interneurons or long-distance signaling via neuropeptides or other modulators (Fig. 5C).”

Fig. 5: Updated to include new cell-specific mec-10 rescue data and revised model.

(5) Do inx-7 or inx-10 rescue in AFD and AIB using cell-specific promoters rescue the behavior?

Yes. We tested this during revision. Using the AFD-specific srtx-1b promoter, we expressed inx10 cDNA selectively in AFD neurons of inx-10 mutant worms. This manipulation significantly restored tactile-dependent locomotion modulation compared to non-transgenic inx-10 mutants (Fig. 6D), demonstrating that inx-10 expression in AFD alone is sufficient to rescue the behavioral defect.

Revisions to the manuscript:

Line 366-370: Added a description of the AFD-specific inx-10 rescue results.

“We next tested whether restoring inx-10 specifically in AFD would be sufficient to rescue the behavioral defect. Using the AFD-specific srtx-1b promoter, we expressed inx-10 cDNA in inx-10 mutant worms. These transgenic animals displayed significantly improved locomotion modulation (∆speed: 42 ± 5%) compared to non-transgenic inx-10 mutants (15 ± 4%; p = 0.018; Fig. 6D), indicating that inx-10 expression in AFD alone is sufficient to restore function.”

Fig. 6D: Updated to include new cell-specific inx-10 rescue data.

(6) How Guanylyl cyclase gcy-18 function is related to the electrical synapse activity between AFD and AIB? Is AFD downstream or upstream of AIB in this context?

At present, the precise relationship between GCY-18 signaling and the AFD-AIB electrical synapse is not fully resolved. Given that AIB receives mechanosensory input from FLP, it is likely that AIB acts upstream of AFD during tactile-dependent locomotion modulation. However, because the AIB-AFD connection is mediated by gap junctions, communication could also be bi-directional, especially since small signaling molecules such as cGMP and Ca²⁺ are known to diffuse through electrical synapses.

We have therefore revised the manuscript to state explicitly that the directionality of information flow between AFD and AIB remains open, and that this will be an important question for future investigation (Line 455-458).

“Together, these findings support a model in which AIB functions as a hub neuron that relays mechanosensory input from FLP to AFD to modulate locomotion (Fig. 5C). However, because electrical synapses are often bidirectional, information flow may also occur in the opposite direction, from AFD to AIB.”

Reviewer #2 (Public review):

Summary:

The goal of the study was to uncover the mechanisms mediating tactile-context-dependent locomotion modulation in C. elegans, which represents an interesting model of behavioral plasticity. Starting from a candidate genetic screen focusing on guanylate cyclase (GCY) mutants, the authors identified the AFDspecific gcy-18 gene as essential for tactile-context-dependent locomotion modulation. AFD is primarily characterized as a thermo-sensory neuron. However, key thermosensory transduction genes and the sensory ending structure of AFD were shown here to be dispensable for tactile-context locomotion modulation. AFD actuates tactile-context locomotion modulation via the cell-autonomous actions of GCY-18 and the CNG-3 cyclic nucleotide-gated channel, and via AFD's connection with AIB interneurons through electrical synapses. This represents a potentially relevant synaptic connection linking AFD to the mechanosensory-behavior circuit.

Strengths:

(1) The fact that AFD mediates tactile-context locomotion modulation is new, rather surprising, and interesting.

(2) The authors have combined a very clever microfluidic-based behavioral assay with a large set of genetic manipulations to dissect the molecular and cellular pathways involved. Rescue experiments with singlecopy transgenes are very convincing.

(3) The study is very clearly written, and figures are nicely illustrated with diagrams that effectively convey the authors' interpretation.

Weaknesses:

(1) Whereas GCY-18 in AFD and the AFD-AIB synaptic connection clearly play a role in tactile-context locomotion modulation, whether and how they actually modulate the mechanosensory circuit and/or locomotion circuit remains unclear. The possibility of non-synaptic communication linking mechanosensory neurons and AFD (in either direction) was not explored. Thus, in the end, we have not learned much about what GCY-18 and the AFD-AIB module are doing to actuate tactile context-dependent locomotion modulation.

We agree with the reviewer that although GCY-18 in AFD and the AFD-AIB connection are clearly required for tactile context-dependent locomotion modulation, the precise mechanisms by which they influence mechanosensory and locomotor circuits remain unresolved. In particular, the possibility of nonsynaptic communication or bidirectional signaling between mechanosensory neurons and AFD cannot be addressed by the current experiments and warrants future investigation.

At the same time, we believe this study reveals several previously unrecognized aspects of tactiledependent locomotion modulation that provide a foundation for future mechanistic investigation.

Specifically, we show that (i) GCY-18 functions in AFD to support tactile-dependent locomotion modulation; (ii) the cGMP-gated channel TAX-4, required for thermosensation, is dispensable for this process, whereas CNG-3 is required, revealing functional specialization within AFD; (iii) the interneuron AIB is necessary for this modulation; and (iv) restoring a single electrical connection between AFD and AIB using mammalian Cx36 is sufficient to rescue tactile-dependent modulation in innexin mutants.

Accordingly, we now explicitly state in the revised Discussion that “a limitation of this study is that the directionality and mode of information flow between AFD and AIB remain unresolved, and defining this relationship will be an important goal for future investigation” (Line 472-475).

(2) The authors only focused on speed readout, and we don't know if the many behavioral parameters that are modulated by tactile context are also under the control of AFD-mediated modulation.

We used locomotion speed as the primary behavioral readout because it provides a robust measure for detecting whether behavior is modified by prior tactile experience, rather than to capture the full spectrum of motor outputs. This strategy is often used to assess experience-dependent behavioral plasticity across sensory modalities and enabled us to uncover the unexpected role of AFD in tactile-dependent plasticity.

In the revised manuscript, we expanded our analysis to include additional behavioral parameters. As described in the Results, AFD-ablated worms showed a complete loss of context-dependent modulation not only in speed, but also in idle time and turning frequency, with no detectable differences between uniform and binary chambers (Fig. 4E). These data strengthen the conclusion that AFD broadly supports tactiledependent behavioral modulation rather than selectively affecting a single locomotor parameter.

Revisions to the manuscript:

Fig. 4E: Revised panel to include additional locomotion parameters, including idle time and turning frequency, in wild type and AFD-ablated worms.

Lines 283–285: Expanded the results to describe changes in locomotion speed, idle time, or turning frequency of AFD-ablated mutant worms. “These animals showed no detectable differences between uniform and binary chambers in locomotion speed, idle time, or turning frequency (Fig. 4E).”

(3) The AFD-AIB gap junction reconstruction experiment was conducted in an innexin double mutant background, in which the whole nervous system's functioning might be severely impaired, and its results should be interpreted with this limitation in mind.

We appreciate the reviewer’s concern that the innexin double-mutant background may broadly affect nervous system function, and we agree that loss of innexins is not restricted to the AFD-AIB synapse and could introduce global circuit perturbations.

Importantly, however, the specificity of the rescue is informative. In an innexin double-mutant background, where electrical coupling is broadly disrupted, re-establishing a single electrical synapse between AFD and AIB using Cx36 was sufficient to restore tactile-dependent locomotion modulation (Fig. 6D). The ability of a targeted AFD-AIB connection to rescue behavior despite the absence of many other electrical synapses argues against a purely global network defect and instead identifies the AFD-AIB electrical synapse as a critical locus for this modulation.

To further address this concern, we performed an additional rescue experiment in a less perturbed genetic background. In the revised manuscript, we show that AFD-specific expression of inx-10 rescues locomotion modulation in inx-10 single mutants (Fig. 6D). Together, these complementary rescue approaches, one restoring endogenous innexin function in AFD and the other reconstituting an electrical synapse using Cx36, support the conclusion that AFD-AIB electrical coupling is sufficient to enable tactile-dependent locomotion modulation, rather than reflecting nonspecific recovery of global circuit function.

Revision to the manuscript:

Fig. 6D and Lines 366-370: Added new data and revised text showing that AFD-specific inx-10 expression restores tactile-dependent locomotion modulation.

“We next tested whether restoring inx-10 specifically in AFD would be sufficient to rescue the behavioral defect. Using the AFD-specific srtx-1b promoter, we expressed inx-10 cDNA in inx-10 mutant worms. These transgenic animals displayed significantly improved locomotion modulation (∆speed: 42 ± 5%) compared to non-transgenic inx-10 mutants (15 ± 4%; p = 0.018; Fig. 6D), indicating that inx-10 expression in AFD alone is sufficient to restore function.”

Reviewer #3 (Public review):

Summary:

Rosero and Bai report an unconventional role of AFD neurons in mediating tactile-dependent locomotion modulation, independent of their well-established thermosensory function. They partially elucidate the signaling mechanisms underlying this AFD-dependent behavioral modulation. The regulation does not require the sensory dendritic endings of AFD but rather the AFD neurons themselves. This process involves a distinct set of cGMP signaling proteins and CNG channel subunits separate from those involved in thermosensation or thermotaxis. Furthermore, the authors demonstrate that AIB interneurons connect AFD to mechanosensory circuits through electrical synapses. They conclude that, beyond its primary function in thermosensation, AFD contributes to context-dependent neuroplasticity and behavioral modulation via broader circuit connectivity.

While the discovery of multifunctionality in AFD is not entirely unexpected, given the limited number of neurons in C. elegans (302 in total), the molecular and cellular mechanisms underlying this AFD-dependent behavioral modulation, as revealed in this study, provide valuable insights into the field.

Strengths:

(1) The authors uncover a novel role of AFD neurons in mediating tactile-dependent locomotion modulation, distinct from their well-established thermosensory function.

(2) They provide partial insights into the signaling mechanisms underlying this AFD-dependent behavioral modulation.

(3) The neural behavior assays utilizing two types of microfluidic chambers (uniform and binary chambers) are innovative and well-designed.

(4) By comparing AFD's role in locomotion modulation to its thermosensory function throughout the study, the authors present strong evidence supporting these as two independent functions of AFD.

(5) The finding that AFD contributes to context-dependent behavioral modulation is significant, further reinforcing the growing evidence that individual neurons can serve multiple functions through broader circuit connectivity.

Weaknesses:

(1) Limited Behavioral Assays: The study relies solely on neural behavior assays conducted using two types of microfluidic chambers (uniform and binary chambers) to assess context-dependent locomotion modulation. No additional behavioral assays were performed. To strengthen the conclusions, the authors should validate their findings using an independent method, at the very least by testing AFD-ablated animals and gcy-18 mutants with a second behavioral approach.

The reviewer points out that the original study relied on locomotion assays in two microfluidic environments (uniform and binary chambers) and suggests validation using an independent behavioral approach, particularly for AFD-ablated animals and gcy-18 mutants.

To address this concern, we developed an independent behavioral assay in which the exploration and assay environments are physically separated by a removable barrier (Figure 1–Supplement 1A). In this design, worms first explored distinct physical settings, after which a barrier was inserted to confine them to an identical assay zone. This approach allowed us to directly test whether context-dependent locomotion modulation can be maintained when worms are prevented from re-entering the exploration environment and must rely solely on prior experience.

Using this assay, we found that wild-type worms that had previously explored environments matching the assay zone moved significantly faster than those that had explored non-matching environments (Figure 1– Supplement 1B-C). These results demonstrate that context-dependent locomotion modulation is retained even when ongoing sensory input from the exploration zone is eliminated, independently validating our original findings using a distinct behavioral paradigm.

Further, using this same assay, we found that locomotion modulation was significantly impaired in both gcy-18 mutants and AFD-ablated worms (Figure 4–Supplement 2A). Together, these results provide independent behavioral evidence supporting the conclusion that AFD and gcy-18 are required for contextdependent locomotion modulation.

Revision to the manuscript:

Figure 1–Supplement 1A: Added schematic and results from the removable-barrier assay in wild type animals.

Lines 120-137: Added corresponding Results text describing the new assay and wild-type behavior.

“Because worms in the binary chamber are exposed to both pillar types and remain free to move between exploration and assay zones, the behavioral differences described above could reflect exposure to a more complex physical environment rather than prior experience alone. To directly test whether locomotion is modulated by prior physical experience independently of continued access to the exploration zone, we designed microfluidic chambers in which the assay zone could be separated from the exploration zone by a removable barrier (Fig. 1–Supplement 1A). In these chambers, worms were initially allowed to explore the entire device, including exploration zones that either matched or differed from the assay zone. A barrier was then inserted to prevent worms in the assay zone from re-entering the exploration zones.

Under these conditions, locomotion immediately after barrier insertion was higher in worms that had previously explored physical settings matching the assay zone (205 ± 8 µm/s) than in worms that had explored non-matching settings (151 ± 7 µm/s; p = 0.006; Fig. 1–Supplement 1B). This difference persisted when worms were recorded 40 minutes after barrier insertion, with animals in matching chamber retaining their higher locomotion rates (218 ± 11 µm/s) compared to those in non-matching chambers (185 ± 8 µm/s; p = 0.02; Fig. 1–Supplement 1B). These findings demonstrate that prior exploration of distinct physical environments can modulate locomotion even when worms are prevented from returning to those environments, supporting a role for prior physical experience independent of ongoing sensory input.” Figure 4–Supplement 2A: Added data for gcy-18 mutants and AFD-ablated worms in the removable barrier assay.

Lines 288-296: Added text describing behavioral defects in gcy-18 mutants and AFD-ablated worms using the new assay.

“Building on our finding that locomotion modulation can be driven by prior physical experience even after worms are prevented from re-entering the exploration zones, we next tested whether AFD is required for this modulation using chambers in which the exploration and assay zones were separated by a removable barrier (Fig. 1–Supplement 1A). Under these conditions, locomotion modulation was significantly reduced in AFD-ablated worms (∆speed: -AFD = 1 ± 6% vs. N2 = 23 ± 7%; p = 0.036; Fig. 4–Supplement 2A). Similarly, gcy-18 mutants showed defective locomotion modulation (∆speed: gcy-18 = -1 ± 8% vs. N2 = 23 ± 7%; p = 0.034; Fig. 4–Supplement 2A). These results indicate that AFD and gcy-18 are required to generate locomotion modulation in response to recent physical experience, even when continued access to surrounding environments is restricted.”

(2) Clarity in Behavioral Assay Methodology: The methodology for conducting the behavioral assays is unclear. It appears that worms were free to move between the exploration and assay zones, with no control over the duration each worm spent in either zone. This lack of regulation may introduce variability in tactile experience across individuals, potentially affecting the reproducibility and quantitativeness of the method. The authors should clarify whether and how they accounted for this variability.

In the primary assay, worms were allowed to move freely between the exploration and assay zones for one hour, and each animal’s tactile experience depended on its exploratory trajectory. To address the resulting variability, we performed an a priori power analysis, which determined that approximately 160 worms distributed across more than 20 chambers per condition were sufficient to obtain reliable populationlevel measurements. This sampling strategy was applied consistently across all experiments. Accordingly, analyses emphasize well-powered population means rather than individual trajectories, ensuring robust and reproducible comparisons despite variability in individual experience.

In addition, as described above, we developed a removable-barrier assay that eliminates variability from ongoing exploration by confining worms to the assay zone after a defined exploration period. The consistency of behavioral effects across both assays further supports the robustness and reproducibility of the approach.

(3) Potential Developmental and Behavioral Confounds in Mutant Analysis: Several neuronal mutant strains were used in this study, yet the effects of these mutations on development and general behavior (e.g., movement ability) were not discussed. Although young adult worms were used for behavioral assays, were they at similar biological ages? To rule out confounding factors, locomotion assays assessing movement ability should be conducted (see reference PMID 25561524).

To address the possibility that behavioral phenotypes in mutant strains arise from developmental defects or impaired general locomotion, we directly measured locomotion speed on agar plates and body length in gcy-18 mutant and AFD-ablated worms. Neither genotype showed defects in basal locomotion speed or body length compared to wild type animals (Figure 4–Supplement 2B-C), indicating that the observed modulation defects are not explained by impaired development or gross motor ability.

To further control for developmental variability, all behavioral assays were performed using agesynchronized populations. Animals were selected at a defined gravid adult stage, identified by the presence of 5-10 eggs arranged in a single row within the gonad. All mutant strains reached this developmental stage approximately three days after egg laying, comparable to wild type animals.

Revision to the manuscript:

Figure 4–Supplement 2B-C: Added quantification of locomotion speed on agar plates and body length for gcy-18 mutants and AFD-ablated worms.

Lines 297-304: Added text describing the data presented in Figure 4–Supplement 2B-C.

“Finally, to determine whether the modulation defects observed in gcy-18 mutants and AFD-ablated worms could be attributed to developmental abnormalities or gross motor impairments, we measured locomotion speed and body length on standard NGM plates. Both day-1 adult AFD-ablated worms (speed: 281 ± 10 µm/s; p = 0.33; body length: 1.12 ± 0.01 mm; p = 0.76) and gcy-18 mutants (speed: 291 ± 13 µm/s; p = 0.22; body length: 1.15 ± 0.02 mm; p = 0.86) showed locomotion speeds and body lengths comparable to wild type controls (speed: 252 ± 30 µm/s; body length: 1.14 ± 0.02 mm; Fig. 4–Supplement 2B, C). These results indicate that the loss of context-dependent locomotion modulation is not due to developmental defects or gross impairments in locomotion.”

(4) Definition and Baseline Measurements for Locomotion Categories: The finding that tax-4 and kcc-3 contribute to basal locomotion but not to context-dependent locomotion modulation is intriguing. The authors argue that distinct mechanisms regulate these two processes; however, the study does not clearly define the concepts of "basal locomotion" and "context-dependent locomotion," nor does it provide baseline measurements. A clear definition and baseline data are needed to support this conclusion.

We define basal locomotion as the locomotion speed of worms measured in the binary chamber, where wild-type animals consistently exhibit lower locomotion rates. Measurements from the binary chamber therefore serve as the baseline reference for locomotion speed in our microfluidic assays. Context-dependent locomotion modulation is defined as the quantified difference in locomotion speed between worms in uniform chambers and those in binary chambers. These definitions are now stated in:

Lines 199-201: “We examined the locomotion speed of mutant worms in the binary chambers, which we refer to as the basal speed because wild type worms consistently move slowest in this environment.”

Lines 645-46: “Asterisks above horizontal black lines indicate statistically significant differences in basal speed, defined as speed of worms in the binary chamber”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The availability of strains has not been mentioned. This should be addressed.

The revised Methods section now includes a complete list of strains used in this study, and we have added a statement indicating that all strains are available upon request.

Minor comment:

Figure 1C - it should be Idle, not Idel.

We have corrected the y-axis label in Figure 1C to ‘Idle.’

Reviewer #2 (Recommendations for the authors):

This is an interesting and well-written article, which I greatly appreciated reading. There are a few concerns that the authors should address, in my opinion, to provide a more complete and convincing story.

Major points:

(1) Maybe the material transmitted to me was incomplete, but I did not find the gcy gene screen results. It seems important to present the screen results in full, together with the description of the alleles tested for the 24 gcy genes.

The revised manuscript now includes the complete results of the gcy mutant screen in Figure 2– Supplement 1, with the alleles tested for all 24 gcy genes listed in Table S1.

(2) I did not find the actual p-values, sample sizes for each condition, or raw data; nor a data availability statement indicating where to retrieve these.

Statistical significance is indicated by asterisks in all figures, with definitions provided in each figure legend (n.s., p > 0.05; *, p < 0.05; **, p < 0.01; ***, p < 0.001). Sample sizes are shown as individual data points in the plots, and we have now added explicit n values to each figure legend for clarity. A Data Availability Statement has also been added to indicate where the raw data can be accessed. Where possible, we have included exact p-values. For analyses using Tukey-Kramer post hoc tests, p-values are reported to four decimal places, reflecting the output limits of the statistical software used.

(3) It is not clear why the authors only quantified animal speed for most of the study. What about idle time, turns, and reversals? This choice limits the reach of the study, as we only partly understand what AFD is doing, notably to explain the phenotype in the preference assay.

Data on idle time, turning frequency, and reversal frequency for wild-type worms are now included in Figure 1F. In addition, we present new data showing that AFD ablation disrupts context-dependent modulation of locomotion speed, idle time, and turning frequency (Figure 4E).

(4) Figure 2D and related text: these conclusions are based on a single mutant analysis. Were the millionmutation project lines outcrossed? It would be much more convincing if more gcy alleles were tested (this should be relatively easy since classical alleles are available at the CGC for gcy-8 and gcy-18).

The million-mutation project lines used in this study were outcrossed prior to analysis. In addition, we confirmed that the observed defects were specifically due to loss of gcy-18 function by rescuing the phenotype through expression of gcy-18 cDNA under AFD-specific promoters. This cell-specific rescue shows that the behavioral defects arise from disruption of gcy-18 rather than from background mutations.

(5) It is hard to interpret the speed phenotype when the authors switch between Delta speed and absolute speed display from one figure to another, or even from one panel to another. If only tax-4 and kcc-3 display a constitutive speed phenotype, then there should be no problem showing the absolute speed data in every panel. This is important to convince the reader that major speed changes in mutants are not biasing the interpretation based on Deltas. Indeed, if some mutants move very fast, there might be a ceiling effect. Conversely, if they move very slowly, there might be a 'sickness' effect. Both effects could prevent seeing a tactile-context-dependent modulation, and the results would need to be interpreted much more carefully. Providing the full view on absolute speed levels would also really help support the whole discussion paragraph about the differential regulation of constitutive versus context-dependent locomotion (from L339 onward).

We focus on ∆speed because it directly quantifies experience-dependent locomotion modulation relative to each strain’s own baseline, making it an appropriate metric for comparing tactile plasticity across genotypes. This approach avoids confounding effects from strain-specific differences in overall locomotion levels.

At the same time, we agree that absolute locomotion speed is important to consider when interpreting behavioral phenotypes. To address this, we added plate-based locomotion speed and body length measurements for two key genotypes that lack modulation, gcy-18 mutants and AFD-ablated worms (Figure 4–Supplement 2B–C). Both exhibit normal locomotion on agar plates, indicating that their defects in tactiledependent modulation are not due to impaired motor ability or general sickness.

In addition, among the mutants tested in microfluidic chambers, tax-4 mutants display elevated basal speed yet retain robust context-dependent modulation, indicating that ceiling effects do not limit detection of modulation.

(6) The gap junction expression is a nice experiment. But there is a major limitation that should be stated: the electrical synapse re-construction is made in a double mutant background in which the whole animal circuitry might be severely affected. It might well be that the restoration of behavioral plasticity represents something totally irrelevant to wild-type nervous system functioning. A cell-specific innexin knockout is needed to fully support the relevance of the AFD-AIB connection.

We agree that reconstruction of an electrical synapse in an innexin double-mutant background carries the limitation that global circuit function may be broadly affected. To address this concern, we performed an additional rescue experiment in a less perturbed genetic background.

As described above, we show that AFD-specific expression of inx-10 is sufficient to restore tactiledependent locomotion modulation in inx-10 single mutants (Fig. 6D). This cell-specific rescue does not rely on a double-mutant background and converges on the same outcome as the Cx36-based electrical synapse reconstruction. Together, these complementary approaches support the conclusion that restoring AFD-AIB coupling is sufficient to enable tactile-dependent locomotion modulation, rather than reflecting nonspecific recovery from global circuit disruption.

(7) How was developmental age controlled? It seems that all genotypes were grown for a fixed duration (72h). Some mutants, like gcy-8, might grow slower. It would be useful to at least provide control data in wildtype animals showing that behavioral performance is similar even in slightly younger animals (covering the developmental age of the youngest mutant).

Developmental age was controlled by strict age synchronization and staging criteria rather than growth duration alone. Worms were synchronized by allowing 40-50 young adults to lay eggs on OP50-seeded NGM plates for two hours, after which adults were removed. Developmental stage was further assessed by gonadal morphology, and only young adult animals with 5-10 eggs arranged in a single row were selected for behavioral assays. Using these criteria, all strains, including mutants, consistently reached the assayed stage approximately three days after egg laying, comparable to wild type animals.

To further address the possibility that subtle developmental differences could influence behavior, we measured locomotion speed on agar plates and body length for genotypes that show defects in contextdependent modulation. gcy-18 mutants and AFD-ablated worms exhibited normal locomotion rates and body size, indicating that their behavioral phenotypes are unlikely to arise from developmental delay or impaired general motor ability. These control data are now included in the revised manuscript (Figure 4– Supplement 2B–C).

(8) Plasmid construction description is entirely lacking.

Description of plasmid construction has been added to the revised Methods.

Minor points:

(1) 'Context-dependent locomotion' should be replaced by 'tactile context-dependent locomotion' or something similar throughout the manuscript when referring to the impact of the pillar environment.

Presently, this phrasing shortcut makes the communication too vague throughout, and even confusing when presenting the result of supplementary Figure 2 (where both thermal and tactile contexts are manipulated).

We appreciate this suggestion and have revised the terminology for clarity where appropriate. Prior to introducing the mechanosensory origin of the modulation (that is, before presenting the mec-10 data), we retain the broader term “context-dependent modulation” to avoid presupposing a tactile mechanism before it is experimentally established.

(2) L97: Suggested change along the same lines: "prior experience" -> "prior tactile experience".

We have made this change as suggested.

(3) Figure 1A: Would the author consider swapping the order of conditions displayed in this diagram? It would make more sense to have the same left-to-right order in the whole figure with the binary chamber on the left, particularly since the author describes the results considering the binary chamber as the 'reference point'.

The order of chambers in Figure 1A has been revised as suggested, with the binary chamber now shown on the left.

(4) Figure 1C: 'idel' typo in the axis label.

The y-axis label has been updated from “idel” to “idle.”

(5) Without AFD-specific manipulations, the data with tax-4 and tax-2 mutants provide limited information regarding TAX-4 and TAX-2 role in AFD. It should be explicitly mentioned in the Results section that they might work in other neurons.]

The revised manuscript now explicitly states that the tax-2(p694) allele affects multiple neurons, including BAG, ASE, ADE, and AFD (Lines 421–422).

(6) L220-222: The strict meaning of this sentence implies that one attributes a role to AFD in controlling constitutive locomotion, but none of the presented data directly shows this (both kcc-3 and tax-4 mutant phenotypes could arise from additional neurons, regardless of any perturbation in AFD). This should be corrected.

To avoid implying that AFD directly controls constitutive locomotion, we have removed the sentence in question, “Together, these findings suggest that the role of AFD neurons in modulating context-dependent locomotion is distinct from their thermosensory functions and differs from the mechanisms controlling basal locomotion”, from the revised manuscript.

(7) L328-329: Overstatement. Without AFD-specific manipulation of TAX-2 and TAX-4, the different mutant phenotypes could be due to different cell types, rather than different protein pairs in the channel heteromers. I would recommend addressing this alternative possibility directly in the discussion, rather than focusing only on one (I agree, very cool) possibility.

We have clarified this point in the revised text. We now explicitly note that the tax-2(p694) mutation affects tax-2 expression in multiple neurons (AFD, BAG, ASE, and ADE) (Lines 421–422).

Reviewer #3 (Recommendations for the authors):

(1) Clarification of inx Gene Expression Analysis (Lines 270-271): The authors should specify how the expression of inx genes in individual neurons was identified.

The revised manuscript now specifies that innexin expression patterns were identified using the CeNGEN single-cell transcriptomic database (Lines 352–354).

(2) Cx36 Expression in AFD and AIB (Lines 287-288): Further clarification is needed on how Cx36 expression was achieved in AFD and AIB.

We have clarified that Cx36 was expressed specifically in AFD using the srtx-1b promoter and in AIB using the inx-1 promoter, as stated in the main text (Lines 372–373) and the Fig. 6 legend.

eLife Assessment

This important study deepens our understanding of how populations of a given species may diverge in their molecular and physiological patterns as a result of adaptation to different thermal regimes. By approaching this question from multiple directions, the authors provide solid evidence for adaptive changes in three strains of the diamondback moth after only three years of experimental evolution, and support the causal involvement of the PxSODC gene in thermal adaptation to both cold and hot temperatures. This work would benefit from more sophisticated phylogenetic analyses, better statistical support, and a more detailed discussion of the differences in the three strains at the pathway level.

Reviewer #1 (Public review):

Summary:

In this manuscript, Lei and co-workers aim to uncover the genetic underpinnings of thermal adaptation across three strains of the diamondback moth (Plutella xylostella) through experimental evolution over three years under three different thermal regimes. They identify systematic differences in trait responses (e.g., survival, fecundity), metabolic profiles, gene expression, and in the amino acid sequence of the PxSODC gene, among others. These results suggest that the diamondback moth has a strong potential for rapid physiological adaptation to different thermal regimes. Overall, this is a comprehensive and generally well-executed study that addresses an important question in the face of ongoing climate change.

Strengths:

The authors employ multiple approaches to identify signatures of thermal adaptation across the three strains, such as trait performance comparisons, metabolomics, transcriptomics, and amino acid sequence comparisons. All these different angles form a convincing picture of the underlying factors that underpin thermal adaptation in this experimental system. The manuscript is also generally well written and easy to understand.

Weaknesses:

I am unable to judge the validity of all aspects of this work; I will focus only on areas within my core expertise.

(1) The authors identify pathways that are enriched in different strain comparisons (Figure 3E), but do not provide a detailed interpretation of these results. It would be great if the authors could explain in more detail how the physiological processes of a cold-adapted strain of this species may differ from those of a warmer-adapted strain.

(2) The authors reconstruct a phylogenetic tree of the PxSODC gene using the neighbor-joining algorithm. The limitations of this algorithm have been known for many years now, especially for sequences separated by long evolutionary distances. According to Wang et al. (2016), the last common ancestor of the species shown in Figure S4C occurred 392-350 million years ago. Given this, I would strongly recommend that the authors infer a phylogenetic tree using model-based methods, such as those implemented in RAxML-NG or IQ-TREE. Also, in the absence of a valid outgroup sequence, I would show the gene tree as unrooted or rooted based on the corresponding species tree.

(3) There is a key piece of the puzzle that is currently missing: the structural mechanism behind the mutational effects described in this study (e.g., Figure 5). The authors could leverage AlphaFold to generate structural models of different mutants and conduct molecular dynamics simulations to examine their conformational dynamics.

References:

Wang, Yh., Engel, M., Rafael, J. et al. Fossil record of stem groups employed in evaluating the chronogram of insects (Arthropoda: Hexapoda). Sci Rep 6, 38939 (2016). https://doi.org/10.1038/srep38939

Reviewer #2 (Public review):

Summary:

In this paper, the authors set out to better understand the genetic mechanisms underlying thermal adaptation in insects. They experimentally evolved diamondback moth (Plutella xylostella) populations - a pest species with a wide distribution - under both hot (12h:12h 32{degree sign}C/27{degree sign}C) and cold (15{degree sign}C/10{degree sign}C) thermal conditions, and conducted phenotypic assays and metabolic and transcriptomic profiling to analyze how populations changed to deal with this thermal stress compared to the nonevolved ancestral population (constant 26{degree sign}C). Phenotypic assays showed that evolved hot populations had increased survival at high temperatures (42-43{degree sign}C) while evolved cold populations had lower freezing points compared to the ancestral population. When measured at the constant 26{degree sign}C conditions, metabolic and transcriptomic profiles of 3rd instar larvae from the evolved population were distinctive from the ancestral population, with a set of overlapping metabolic and transcriptomic pathways that were significantly differentially expressed in both hot and cold evolved populations compared to the ancestral. The authors narrowed down this set of candidate genes further by focusing on genes with high expression levels overall, whose expression profile was correlated with differentially expressed metabolites, and that contained mutants in both hot and cold strains. From this set, they chose the PxSODC gene for further functional validation, as it has previously been shown to be involved in the response of insects to abiotic stress with its antioxidative role in cellular defense. At the constant 26{degree sign}C, this gene showed lower expression across development in evolved strains compared to the ancestral population, while it showed similar expression patterns under thermal stress. Knockdown of PxSODC resulted in decreased survival rates at high temperatures and higher freezing points compared to the ancestral population. Based on this validation, the authors hypothesize that the non-synonymous mutation in the PxSODC gene that they found in the cold and hot evolved populations might alter the conformation of the PxSODC protein, increasing enzyme capacity. Their experimental evolution experiment furthermore indicates the capacity of the pest species, the diamondback moth, to adapt to a wide range of temperatures, providing insights into its capacity for global dispersal.

Strengths:

(1) The authors did a tremendous amount of work to characterize the mechanisms underlying thermal adaptation in the diamondback moth, artificially selecting populations for three years in the lab and characterizing how they evolved as a result at different biological levels: from phenotypes in different life stages, to larval metabolites and gene transcription, to functionally validating how one of the resulting gene candidates influences the capacity to deal with thermal stress.

(2) The paper identifies and provides further evidence for candidate genetic mechanisms that might be particularly important for thermal adaptation in insects, including lipid metabolism, oxidoreductase activity, and DNA methylation. It is furthermore interesting that the authors found similar mechanisms to be involved in both the adaptation to cold and hot environments. Their functional validation of some of the genes involved in these mechanisms is very useful to understand how these genes might be causally involved in insect thermal adaptation.

(3) The paper also has applied value: the diamondback moth is a pest species with a wide distribution, so understanding its adaptive capacity to different thermal environments is important for predicting the prevalence and potential further range expansion of this species under future climate change.

Weaknesses:

(1) The paper in its current form is hard to digest and would benefit from improved clarification of the storyline, as well as a tighter integration between the phenotypic, omics, and functional validation data. Currently, it is not always clear what the relevance is of all the reported results, nor why certain decisions were made, or how all the different methods the authors used fit together. For example, the authors functionally validated a second gene, PxDnmt1, but it is unclear why this particular gene was chosen, nor how it relates to their selection regimes when looking at the results obtained with the phenotyping and omics data collection. Seeing how much work the authors did, this makes the paper overwhelming and difficult to read.

(2) The authors at times stretch their results too far, as the ecological relevance of their study design and results is not clear, limiting the generalizability and value of the results for understanding species' adaptive potential under climate change. For example, the selection regimes used present the minimum and maximum known temperatures at which the species can survive and develop, but it is unclear how the temperatures relate to the natural environment of the source population, to what extent wild populations might experience these temperatures, and whether they would experience them at the extended duration used (12h at max/min temperature). Moreover, I wonder whether the comparisons made would identify the genes that matter under natural conditions, as unevolved populations were kept under constant conditions compared to 12h:12h temperature regimes for the evolved populations, and the metabolic and transcriptomic profiling was done under a constant favorable 26{degree sign}C rather than under thermal stress in a, as far as I can tell, randomly chosen life stage (larval stage).

(3) The paper in its current form does not adequately describe the statistical analyses underlying the results, nor do the authors share their code, making it very hard to judge whether the analyses used are appropriate and the results trustworthy. I have concerns about the inappropriate use of t-tests, the lack of correcting for confounding variables, and the need for multiple testing corrections.

Author Response:

Public Review:

We thank you and the reviewers for the thoughtful and constructive comments. The feedback helps us strengthen the manuscript substantially, and we plan to address the key points in the revised version as follows.

Reviewer #1 (Public review):

First, in response to the request for a clearer biological interpretation of the pathway enrichment results, we will expand the Discussion to more directly integrate these findings with the observed life-history divergence between strains.

Second, we agree with the concern regarding the phylogenetic inference of PxSODC. We will therefore re-infer the phylogeny using a model-based Maximum Likelihood approach implemented in IQ-TREE, and, in the absence of an appropriate outgroup, the revised tree will be presented as unrooted.

Third, to address the suggestion for a structural explanation of the mutational effects, we will add new structural analyses using AlphaFold modeling and 100 ns molecular dynamics simulations of the wild-type and mutant PxSODC proteins across three physiologically relevant temperatures.

Reviewer #2 (Public review):

First, we will restructured the Results and streamlined the presentation to better emphasize the central narrative. Extensive descriptive datasets will be moved to the Supplementary Materials, and the rationale linking different analytical layers will be stated more explicitly.

Second, we will also revise the manuscript to better frame the ecological relevance and limitations of the experimental design. Specifically, we will clarify that the thermal selection regimes were chosen to reflect ecologically relevant extremes for the source population from subtropical Fuzhou, where summer and winter temperatures can approach the ranges used in the experiment. We will further explain that the cycling temperature treatments were designed to approximate severe but naturally occurring diurnal fluctuations.

Third, in response to concerns about statistical rigor and reproducibility, we will substantially expanded the statistical methods throughout the manuscript. The revised version will provide a clearer description of the analyses used for each dataset, including sample sizes, comparison structure, and statistical thresholds. We will also clarify the application of multiple-testing correction for both transcriptomic and metabolomic analyses, specified the criteria used in network analyses, and more clearly distinguished the statistical approaches used for pairwise versus multi-group comparisons.

eLife Assessment

This is a potentially important work on the organization of visual information in the rodent superior colliculus. It reports that the selectivity of neurons to line orientation and motion in the visual image is largely governed by the sensitivities of retinal neurons and their ordered projection to the superior colliculus. If confirmed, these conclusions could substantially revise prior thinking in this field. However, in the present state, the methods and analysis are incomplete and cannot justify all the claims.

Reviewer #1 (Public review):

Summary:

When contemplating the role of any sensory area in the brain, an essential question is: How much of the neural code is inherited from the inputs versus constructed de novo by the local circuitry? This study tackles that important question for the case of the mouse superior colliculus (SC), a visual brain area that receives direct input from the retina. The specific aspects of the neural code are the representation of line orientation and direction of motion in the visual image. Over the past 10 years or so, there have been reports that the preferred directions and orientations of neurons vary systematically across the SC in a global map that is not present in the retina, and therefore computed locally.

Here, the authors revisit this question by expanding the range of measurements: They record from the axonal boutons of retinal ganglion cells in the input layer of the SC, from the post-synaptic neurons there, and from neurons in deeper layers of the SC. They conclude that at any given location in the SC, the signals in retinal boutons recapitulate the tuning of retinal ganglion cells, and that SC neurons follow that organization, though it is lost in the deeper layers. Notably, they find no evidence for a global map of these response properties other than what is contributed by retinal input.

Strengths:

The study combines multiple recording methods - calcium imaging and electrical recording - to capture the activity of retinal inputs to the colliculus, the tuning of neurons in the superficial layers close to the input, as well as neurons in deeper layers. Furthermore, the work connects to the recent literature on gradients of tuning properties among retinal ganglion cells. All these set the stage for testing the correspondence between retinal inputs and collicular outputs.

Weaknesses:

The methods used to identify direction-selective and orientation-selective neurons based on visual responses are overly permissive and don't match common usage in this research area. Furthermore, the measurements covered only a small fraction of the visual field, which limits their ability to distinguish between different hypotheses for the global map of visual response properties. Relatedly, the claim that retinal input patterns explain much of the layout in the superior colliculus should be made more quantitative.

Reviewer #2 (Public review):

In this study, the authors investigate the spatial organization of direction and orientation selectivity in the mouse superior colliculus (SC) and its retinal inputs. By combining two-photon imaging of retinal boutons and SC neurons with Neuropixels recordings, they assess whether tuning preferences form structured maps or are arranged in a salt-and-pepper fashion. They further compare SC tuning organization to previously described retinal geometric models to determine the extent to which collicular responses inherit retinal topography. The authors conclude that SC inherits a cardinally biased topographic scaffold from the retina, which progressively weakens with depth, and that strong global maps are absent.

A major strength of the study is the impressive combination of methodologies, including imaging of retinal boutons, imaging of SC neurons, and large-scale electrophysiological recordings across SC depth. The direct comparison to retinal geometric models is particularly valuable, as it situates the SC within a broader framework of retinotopic information transfer and advances our understanding of how retinal computations are transformed in downstream targets.

A limitation of the study, however, is that the imaging experiments sample only a relatively small and spatially homogeneous region of the visual field, whereas the electrophysiological recordings cover a different portion of SC. This separation makes it difficult to form a fully integrated, global picture of the spatial organization of direction and orientation selectivity across the entire collicular map.

Reviewer #3 (Public review):

Summary:

The authors studied the organisation of orientation and direction-selective retinal ganglion cells' boutons in the mouse superior colliculus. They confirmed the results already published (Molotkov, 2023; de Malmazet, 2024; Vita, 2024; Laniado, 2025), that retinal ganglion cells' boutons in the superior colliculus conserve the retinal organisation. Thereby, orientation and direction preferences of retinal boutons at each collicular location reflect the tuning of retinal ganglion cells found at the corresponding retinal location, that is covering a matching receptive field location.

The authors also studied the organization of orientation and direction-selective neurons in the superior colliculus. They report a lack of functional organisation in the superior colliculus for neurons preferring the same stimulus orientation or direction of movement. This goes against several published reports (Ahmadlou and Heimel, 2015; Liang et al., 2023; De Malmazet et al., 2018; Feinberg and Meister, 2014; Kasai and Isa, 2021; Li et al., 2020) but echoes a study from Chen et al. (Chen, 2021). The latter authors contested the strength of the anatomical clustering of tuned alike direction-selective neurons. They found, however, that in about a quarter of their recordings, direction-selective cells with similar preferred directions did cluster anatomically in the superior colliculus.

Here, the authors of the current manuscript under review report that local clustering of tuning was weak in all neural populations and confined to very small spatial scales (10-20 μm). This is one order of magnitude smaller than previously reported clusters of around 100-300μm wide. Therefore, the authors conclude that orientation and direction tuning in the mouse superior colliculus follows a salt and pepper organisation.

Strengths & Weaknesses:

Although the authors performed a solid analysis contesting the functional clustering of direction and orientation selective neurons, there seemed to be some elements in their data in favour of a functional clustering of neurons.

As an illustration, the authors plotted in Figure 1Q the distribution of preferred orientations from all their recorded orientation-selective cells. The curve shows a clear bias, indicating that neurons preferring horizontal orientations were found two times more often than neurons encoding any other orientations. Moreover, the authors recorded all their neurons from a defined anatomical location of the colliculus, marked by the dotted rectangle in Figure 3A-C. Therefore, this suggests that orientation-selective cells in this particular collicular location are biased towards preferring horizontal orientations. This supports an anatomical clustering of tuned alike orientation-selective cells in the superior colliculus.

Similarly, Figure 1P shows a bias in the preferred directions of direction-selective neurons in the same recording area. Cells tended to respond more to upward and forward-moving stimuli. The bias is more modest than the one described above for preferred orientations. However, it still seems significant. For example, cells preferring upwards movements appeared to be four times more abundant than cells preferring downward movements. As a consequence, it indicates that preferred directions might not be uniformly distributed and equally represented across the superior colliculus.

These anatomical biases are also visible in the receptive field analysis of the paper. In Figure 3G, the authors plotted the distribution of preferred orientations for every 10-degree bins within the recorded field of view. Out of 26 bins containing more than one neuron, only 6 seemed to include cells not overwhelmingly preferring a single orientation. These were located towards the top right of the figure. Therefore, over almost 80% of the recorded superior colliculus, the data seem in agreement with the view that orientation-selective cells tend to prefer the same orientation at a given receptive location.

The patch analysis in Figures 4G and H also seems to show some degree of coherence in the preferred orientation and direction of neighbouring tuned collicular cells. In both Figures 4 G and H, clear patches of similar preferred orientation and direction appeared to emerge. For example, in Figure 4H, there is a predominance of horizontally tuned patches. This was expected given the recording bias consisting of a majority of horizontally tuned cells. In addition, vertical and 45-degree patches are also visible, in blue and red, respectively. These patches overlap with the corresponding retinotopic locations in Figure 3G, where the histograms show that cells tend to prefer the same orientations, horizontal, vertical or 45 degrees.

It is important to note that in the previous studies on functional clustering of orientation and direction, variability in the tuning of cells within clusters was always reported (Ahmadlou and Heimel, 2015; Chen et al., 2021; De Malmazet et al., 2018; Feinberg and Meister, 2014; Kasai and Isa, 2021; Li et al., 2020). This was more marked for direction-selective cells than for orientation-selective cells. In general, cells preferring all four cardinal directions were often recorded at any given collicular location. Similarly, orientation-selective cells could be found to prefer deviant orientations compared to adjacent cells. Therefore, it is not surprising to see locally mixed tuning in collicular neurons. However, what appeared significant in these studies was the overall proportion of cells with similar tuning in patches of the superior colliculus. As described above, this also seems to be the case in the data of this manuscript.

To conclude, it seems that authors tend to overlook the sources of agreement between their data and previous reports showing functional clustering of cells in the superior colliculus. Instead, the authors tend to emphasise the dissimilarities and variability to put forward a contentious view on the organisation of orientation and direction selectivity in neurons of the superior colliculus. This, I fear, is detrimental to the field because it creates a sort of manufactured chaos that produces unnecessary confusion for readers who do not attentively read the manuscript. It would be valuable for the authors to consider rewriting the manuscript, acknowledging where their data, in fact, support some level of functional clustering.

Author Response:

We thank the reviewers and editors for their thoughtful and constructive assessment. We are encouraged that the reviewers viewed the combination of retinal bouton imaging, collicular neuron imaging, and depth-resolved electrophysiology, together with the comparison to retinal geometric models, as a strength of the study. As the reviewers note, our findings are consistent with previous in vitro studies showing topographic organization of tuning in the retina and with recent work demonstrating the precision of retinotopic mapping from retina to superior colliculus (SC). In revision, we will refine our definition of tuning, sharpen our claims about the spatial organization across SC and its correspondence to retinal topography, and make clearer our aim of reconciling seemingly opposing findings in the literature. In addition, we will provide a detailed response to all other points raised by the reviewers.

A central point raised in the reviews concerns our definition of direction- and orientation-selective cells. We agree that relying only on statistical significance is not sufficient for our purposes, because the resulting classification can depend on recording duration and statistical power. In the revised manuscript, we will therefore introduce thresholding criteria for direction and orientation selectivity indices (DSI and OSI) in addition to significance-based testing. We will also make clearer that our primary question is which stimulus directions and orientations are represented at a given receptive field location, rather than the distribution of preferences among neurons classified as purely direction- or orientation-selective.

We will also revise the text to define more precisely what our data do and do not establish about the large-scale organization across SC. Our intended conclusion is not that we identify a novel global organization, which would require sampling a larger portion of visual space, but rather that the regions we sampled are not well explained by previously proposed global maps in which each visual field location is dominated by a single tuning preference and the same organization is conserved across individuals. Instead, our data are more consistent with a retinal organization of biases toward specific directions and orientations that vary systematically across visual space.

We will further clarify how we quantified the correspondence between our data and the previously established retinal model of direction and orientation tuning. In the current manuscript, we report the errors between model predictions and measured tuning preferences at the corresponding visual field locations. We then assess model performance by comparing the distribution of these errors with the errors obtained from two surrogate datasets: one in which the correspondence between visual field location and tuning preference is destroyed, and one in which the prior distribution of tuning preferences is assumed to be uniform. In the revised manuscript, we will make the interpretation of this comparison more explicit, so that the reported errors are clearly presented as the relevant effect-size measure alongside significance.

Finally, we appreciate the reviewers’ concern that the manuscript may currently emphasize disagreement with previous studies too strongly. We will revise the Discussion to better acknowledge where our data support some degree of local bias or weak clustering, while clarifying that we do not find evidence for a robust, stereotyped global map that is consistent across animals. Our goal is to sharpen the manuscript so that it better reconciles seemingly divergent findings in the literature rather than setting them in opposition.

eLife Assessment

This important study advances our understanding of the neural substrate of planning trajectories towards a goal by using recurrent neural networks. The manuscript provides solid evidence for most of the claims, but it remains unclear whether the dynamics do indeed bear the defining characteristics of attractors, and the interpretation and scope of some claims may need to be reassessed in light of prior work. The work will be of broad interest to theoretical and systems neuroscientists and to cognitive scientists.

Reviewer #1 (Public review):

Summary:

This work builds a theory to implement planning trajectories towards a goal in a known environment, inspired by analyses of prefrontal neural recordings. Unlike standard neural architectures for this task, such as value-based learning and successor representations, their proposed theory is able to adapt to novel goal locations within a trial. The key to the theory is that future times are represented by orthogonal groups of neurons. The recurrent connectivity between groups of neurons selective to specific future times and locations reflects the learned knowledge of the task. Finally, the authors show that standard networks trained on the task approximate their proposed theory.

Strengths:

The structure of the work is clear, and the presentation of the results is very well written, which is particularly noticeable given the consequential amount of results presented. The authors are able to link their theory with experimental findings in neural recordings. The reverse-engineering of trained recurrent neural networks is very thorough, by analyzing both dynamics and connectivity. The assumptions and predictions of their model are clearly stated.

Weaknesses:

It is unclear whether their proposed theory, "space-time attractors", actually is an attractor network. The authors used recurrent neural networks with very few timesteps, and long single neuron time constants with respect to the task time scales. Attractor networks, as the ones the authors cite, refer to networks that generate nontrivial patterns of activity through recurrent interactions, after long periods of time.

The authors gloss over how the reward inputs are calculated. Computing these reward inputs should be part of the planning process, and the authors are implicitly leaving this problem aside. How does the reward input, which includes future time and location, depend on the actions that have not yet been taken by the agent? It feels like most of the planning computation is already provided by these reward inputs at the beginning of the trial. It could be that the network is only learning to process the planned sequence of actions present in the inputs.

Reviewer #2 (Public review):

This well-written manuscript proposes to use attractors in space and time (STA) as a mechanistic explanation for planning in the prefrontal cortex. The main conceptual hypothesis is that planning is implemented as attractor dynamics in a representation that encodes states at each time step jointly. Depending on inputs, the network relaxes to a trajectory that already contains future states that will be visited at each time step, rather than computing a scalar value at each point in time and space like other classical approaches from RL. The authors compare this approach to implementations such as TD learning and successor representation, and further show that trained recurrent neural networks on specific tasks involving planning develop structured subspaces resembling the ones postulated in STA.

The idea of treating attracting trajectories unfolding in time as the computational substrate for planning is very interesting and potentially important. The explicit construction of a state x time representational space and its implementation via recurrent dynamics are appealing and convincing in the idealized tasks considered. I found the manuscript to be refreshingly explicit regarding several of the assumptions and limitations of the models, for example, the fact that certain advantages can be viewed as properties of the state space itself and not necessarily of a fundamentally new planning mechanism.

Overall, the manuscript presents a cool attractor model that extends in time and explores its performance in a subset of illustrative tasks involving planning. My doubts concern mostly the interpretation and scope of the claims made in the manuscript. Here are a few comments where I detail my questions/concerns:

(1) The authors nicely discuss that much of the difference between STA and classical TD or SR agents is "in some sense a property of the state space rather than the decision making algorithm," and that TD and SR could in principle be implemented in a comparable space x time representation. This is fair, but it also suggests that the central contribution of the manuscript lies primarily in the representational factorization (state x time tiling) and its dynamical implementation via attractors, rather than in a fundamentally new planning algorithm or theory, mechanistic or not. I think theory should be distinguished from mechanism, and it would therefore help the reader to describe the conceptual advancement more as a novel mechanism or implementation than a novel (mechanistic) theory for decision/planning.

(2) Related to my previous point, I think it would be helpful to position STA more explicitly relative to computational/theoretical literature in which attractor networks encode temporally ordered patterns (so effectively including future times). For example, classical extensions of Hopfield networks with asymmetric connectivity implement retrieval of sequences and ordered transitions between patterns (Sompolinsky & Kanter, 1986). More recently, sequential attractors and limit-cycle dynamics have been constructed in structured recurrent networks by the Morrison group (Parmelee et al., 2021). These works do not implement an explicit discretized state x future-time tiling as in STA and do not specifically discuss the usage for planning. However, they do provide concrete precedents for attractor dynamics over temporally structured trajectories in terms of mechanism. It would be useful to discuss this literature and clarify a little what's new mechanistically in the view of the authors.

(3) A central claim of the manuscript is that space-time trajectories are attractors of the STA dynamics. The manuscript does provide empirical evidence consistent with attractor-like behavior. However, it is not explicitly shown whether trajectory representations persist in the absence of sustained external inputs. So it's not clear to me whether the trajectories should be interpreted as intrinsic attractors of the recurrent system, which can be selected by delivering transient inputs, or whether they must be stabilized by a specific continuous external drive. It would be useful if the author could clarify/discuss this point.

As far as I understand it, reward information is provided as input to specific populations encoding future time steps, and that's essential for rapid adaptation without rewiring connectivity. How such future-time-specific reward inputs would be generated and routed to distinct neural populations isn't entirely clear to me. Since this seems to be an essential component of the model, I think it would be important to discuss more deeply the source and plausibility of these reward signals related to different timesteps.

(4) The authors note that vanilla STA scales linearly with planning horizon, and discuss potentially hierarchical extensions for longer horizons. They acknowledge that learning abstractions remains an open challenge, yet the examples of planning in the manuscript are restricted to very short temporal horizons and limited branching complexity. It is not obvious to me in what cases the current implementation and interpretation of STA remains viable (for example, in terms of relaxation iterations) as the horizon and branching factor increase. Relatively simple planning can be managed by simpler, less costly models/algorithms, whereas complex planning is a lot harder to deal with, and it's something that a mechanistic "theory" should address. In the context of the claims of the paper in its present form, I think this is possibly the most important conceptual and practical limitation in the manuscript.

(5) The RNN analyses show that trained networks develop structured subspaces aligned with future time indices and exhibit perturbation behavior consistent with attractor-like dynamics. The manuscript also explicitly notes differences between the trained RNN and the handcrafted STA (e.g., long-range couplings between subspaces and differences in behavior of lower-value trajectories under perturbation), which I much appreciated. My doubt is on the specificity of this result, as trained RNNs on fixed-horizon tasks can develop latent dimensions correlated with temporal progress within a trial or time-to-goal. I think it would help the reader to clarify whether the results demonstrate that STA-like computations emerge in RNNs trained on planning tasks, or that RNNs generally develop some kind of structured spacetime representations when tasks involve future timesteps and some degree of flexibility in the decisions.

A few more minor points, mainly concerning clarity:

(1) The main dynamical equation combines a log-domain recurrent term, a floor operation, and a log-sum-exp normalization step, followed by exponentiation. The intuition/logic behind this specific formulation could be clarified for the reader. For example tt would be helpful to explain why the recurrent input appears inside a log, and also whether/how these operations relate to any multiplicative constraint.

(2) While the computational cost of successor representation in an expanded NT x NT representation is discussed, the corresponding scaling of STA in terms of number of units and connections (as a function, for example, of the planning horizon) isn't clear to me. Perhaps the authors could compare costs more explicitly.

(3) In the RNN analyses, structured subspaces aligned with future time indices are shown. I couldn't find a quantification of how much variance is captured by the subspaces, relative to other latent dimensions. Adding it would help get a feeling for the strength of the alignment.

eLife Assessment

This important study presents evidence that the Chromatin-linked adaptor for MSL complex proteins (CLAMP) GA-binding transcription factor (TF) regulates ~75% of HS-induced repression in Drosophila and suggests that CLAMP is the first known transcription factor to induce heat-stress-mediated repression of gene expression. While mechanistic details remain to be sorted out, this manuscript provides convincing evidence that novel pathways involving the CLAMP transcription factor repress gene expression during heat shock stress.

Reviewer #1 (Public review):

Summary:

This work aims to identify the transcription factor responsible for targeting constitutively active genes for repression during heat stress. While the mechanisms underlying heat-stress-induced gene activation are well characterized - primarily involving Heat Shock Factor (HSF), the GA-binding factor GAF, and RNA Polymerase II pausing regulators - far less is known about how repression of constitutive genes is directed. Because known activation factors such as HSF and GAF do not account for repression, the authors sought a DNA-binding factor that could selectively target these genes. They focused on CLAMP (Chromatin-linked adaptor for MSL complex proteins) for several reasons. First, CLAMP recognizes GA-rich DNA motifs similar to those bound by GAF, suggesting it could compete with GAF at regulatory elements and shift transcriptional outcomes. Second, CLAMP has been shown to antagonize GAF binding in certain genomic contexts, suggesting it could counteract activation mechanisms. Third, CLAMP interacts with Negative Elongation Factor (NELF), a factor known to regulate transcriptional repression during heat stress. Finally, CLAMP promotes long-range chromatin interactions, indicating it may influence local chromatin architecture during the heat-stress response. Together, these properties led the authors to hypothesize that CLAMP helps mediate heat-stress-induced transcriptional repression of constitutively active genes.

To test this hypothesis, the authors use immunofluorescence along with three techniques: (1) nascent RNA-sequencing (SLAM-seq) to define the function of CLAMP in heat stress-induced transcriptional activation and repression; (2) Micro-C to identify CLAMP-dependent and independent genome-wide, high-resolution local changes in chromatin organization after heat stress, and (3) HiChIP to identify CLAMP-bound 3D chromatin loop anchors associated with heat-stress-dependent transcriptional regulation.

Analysis of heat-shocked salivary glands or KC cells showed results that aligned across all experiments, indicating that CLAMP is the primary repressor of gene activation upon heat shock. CLAMP also inhibits chromatin loop formation.

Strengths:

The techniques used here are comprehensive, and impressively, the data is unambiguous.

Weaknesses:

These techniques do not reveal the molecular mechanisms, but the authors provide a strong rationale and molecular hypotheses for future studies to dissect.

Reviewer #2 (Public review):

In this manuscript, Aguilera et al. investigate the mechanisms underlying transcriptional repression of constitutively expressed genes during heat stress. While the activation of heat-shock genes has been extensively studied, the mechanisms responsible for widespread transcriptional repression remain poorly understood. The authors propose that the GA-binding transcription factor CLAMP acts as a major regulator of heat-stress-induced transcriptional repression in Drosophila. Using nascent RNA-sequencing approaches, they report that CLAMP contributes to the repression of a large fraction of genes whose transcription decreases upon heat stress. In addition, the authors generate high-resolution Micro-C datasets to analyze changes in chromatin architecture during heat stress and report widespread alterations in chromatin looping associated with transcriptional changes. Based on these results, the study proposes that CLAMP regulates repression through both direct transcriptional mechanisms and modulation of local 3D genome architecture.

The study addresses an important question in gene regulation: how transcription is rapidly repressed during environmental stress. The work is timely because most previous studies have focused on transcriptional activation of heat-shock genes, whereas repression mechanisms remain comparatively less understood. The integration of transcriptional profiling with high-resolution chromatin conformation data is a major strength of the manuscript and provides a valuable resource for the community studying genome organization and stress responses.

The nascent RNA-sequencing experiments appear carefully designed and allow the authors to capture rapid transcriptional responses to heat stress. These data provide convincing evidence that heat stress leads to widespread transcriptional repression of constitutive genes and that CLAMP contributes substantially to this process. The genomic analyses linking CLAMP binding to repressed genes are also informative and support the idea that CLAMP plays a direct regulatory role at many loci.

Another strength of the study is the generation of Micro-C datasets under heat stress conditions. These datasets provide a high-resolution view of chromatin architecture and reveal dynamic changes in local chromatin looping associated with transcriptional responses. The authors' analysis suggests that heat stress induces widespread reorganization of chromatin contacts, and that CLAMP may contribute to these structural changes. This dataset is likely to be useful for future studies exploring how environmental cues influence genome organization.

Despite these strengths, several aspects of the study would benefit from further clarification. First, the mechanism by which CLAMP mediates transcriptional repression remains insufficiently defined. While the data support a role for CLAMP in the repression of a subset of genes during heat stress, the molecular basis of this effect is not fully explored. Second, although the Micro-C dataset represents a valuable resource for studying chromatin architecture during heat stress, the functional interpretation of the observed structural changes could be further developed. In particular, it would be helpful to better establish the relationship between the identified chromatin loops and gene regulation, and to clarify whether these structural changes play a causal role in transcriptional repression or instead reflect broader chromatin reorganization associated with the stress response.

Reviewer #3 (Public review):

Summary:

Exposure to heat shock results in major changes to gene expression programs within the cell, and over the past decades, there has been extensive characterization of the mechanisms through which heat shock activates transcription. However, heat shock also leads to widespread repression of many genes, and the transcriptional mechanisms that mediate this repression have not been well understood. Here, the authors show that the transcription factor CLAMP mediates this heat shock-dependent repression via changes in local 3D chromatin looping. Intriguingly, CLAMP is already bound to chromatin prior to heat shock, but is necessary for the loss of local chromatin loops at its bound sites and repression of genes located within the loops. This study is significant because it defines chromatin looping, depending on a key transcription factor CLAMP, as the major mechanism through which genome-wide changes in gene repression occur in response to an inducible stimulus, heat shock.

Strengths:

The use of the SLAM-seq and Micro-C techniques to measure the necessity of CLAMP for heat shock-dependent transcription repression and local chromatin looping is excellent, and these approaches provide valuable insight into the role of CLAMP in heat shock-dependent repression that was not apparent with older approaches. The HiChIP approach provides an excellent method to test whether CLAMP is bound at sites where there are changes in looping upon heat shock, providing good support for their conclusions that CLAMP induces heat shock repression by decreasing loops. Appropriate controls are present, and there is robust statistical analysis of the bioinformatics data.

Weaknesses:

The study does not provide insight into how CLAMP mechanistically affects loops upon heat shock, although the discussion raises the possibility that this could result from biophysical changes since CLAMP is an intrinsically disordered protein.

eLife Assessment

This study investigates how the HIV inhibitor lenacapavir influences capsid mechanics and interactions with the nuclear pore complex. It provides important insights into how drug-induced hyperstabilization of the viral shell can compromise its structural integrity during nuclear entry. The modeling is technically sophisticated, and the analyses provide solid support for the mechanistic conclusions.

Reviewer #1 (Public review):

The paper from Hudait and Voth details a number of coarse-grained simulations as well as some experiments focused on the stability of HIV capsids in the presence of the drug lenacapavir. The authors find that LEN hyperstabilizes the capsid, making it fragile and prone to breaking inside the nuclear pore complex.

I found the paper interesting. I have a few suggestions for clarification and/or improvement.

(1) How directly comparable are the NPC-capsid and capsid-only simulations? A major result rests on the conclusion that the kinetics of rupture are faster inside the NPC, but are the numbers of LENs bound identical? Is the time really comparable, given that the simulations have different starting points? I'm not really doubting the result, but I think it could be made more rigorous/quantitative.

(2) Related to the above, it is stated on page 12 that, based on the estimated free-energy barrier, pentamer dissociation should occur in ~10 us of CG time. But certainly, the simulations cover at least this length of time?

(3) At first, I was surprised that even in a CG simulation, LEN would spontaneously bind to the correct site. But if I read the SI correctly, LEN was parameterized specifically to bind to hexamers and not pentamers. This is fine, but I think it's worth describing in the main text.

Comments on revisions:

I found that the authors addressed my concerns satisfactorily. The other reviewer raised a number of important points regarding the nuances of the model and the interpretation of the simulations, which the authors rebutted. I think the paper in its current form now is a worthwhile addition to the literature.

Reviewer #3 (Public review):

I have carefully reviewed the manuscript, the two referee reports, and the authors' detailed responses. I appreciate the substantial effort the authors have invested in addressing the reviewers' comments, and I also recognize the strength and ambition of the work. This is a technically sophisticated study that integrates coarse-grained modeling with live-cell imaging to address an important and timely question regarding HIV-1 capsid inhibition by lenacapavir.

Embedded within Reviewer #2's report are several substantive points that warrant careful consideration, particularly with respect to framing, terminology, and engagement with the broader literature. I view my role here is to distinguish those issues from claims that I do not find to be supported.

First, I do not agree with Reviewer #2's central assertion that the manuscript lacks novelty or fails to present meaningful new findings. While individual elements of the system studied here-capsid docking at the NPC, lenacapavir-induced capsid hyperstabilization, capsid rupture, and competition with FG- nucleoporins-have been observed previously, this work provides a coherent, mechanistic account of how these elements are coupled. In particular, the proposed sequence linking LEN-induced lattice hyperstabilization, preferential pentamer loss at the narrow end, NPC-induced mechanical stress, and failure of nuclear import represents a nontrivial integration that goes beyond prior phenomenological observations. I therefore do not view this work as redundant with existing literature.

That said, Reviewer #2 is correct to note that the manuscript would benefit from broader and more explicit engagement with recent independent studies, including computational and hybrid modeling efforts that address capsid mechanics, nuclear entry, and LEN effects using different frameworks. While the authors' bottom-up coarse-grained approach is clearly distinct and, in many respects, more systematically derived, eLife readers would benefit from a clearer discussion of how the present results relate to, complement, or differ from these other approaches. I strongly encourage the authors to add a short discussion paragraph situating their work within this broader context, without disparaging alternative models.

Second, I find that some mechanistic claims in the manuscript would benefit from more careful language distinguishing model-conditioned interpretation from de novo prediction. This applies in particular to discussions of LEN binding heterogeneity and stoichiometry, as well as to conclusions drawn from biased enhanced-sampling simulations. While I agree with the authors that parameterization does not invalidate mechanistic insight, it is important to be precise about what aspects of the behavior emerge from the simulations versus what is constrained by prior experimental knowledge. Modest tightening/revising of language (e.g., "suggests," "is consistent with," "within the model") would address this concern without weakening the scientific conclusions.

Third, Reviewer #2 raises a legitimate semantic issue regarding the use of the term "elasticity." The manuscript infers changes in capsid mechanical response using heterogeneous elastic network models, which quantify effective stiffness and deformability rather than elasticity in the macroscopic materials sense. I recommend that the authors clarify this definition explicitly in the text to avoid confusion and unnecessary debate.

Finally, I note that several of Reviewer #2's objections-particularly those asserting circular reasoning, misuse of enhanced sampling methods, or invalidity of coarse-grained predictions-reflect a misunderstanding of contemporary bottom-up coarse-grained modeling rather than genuine methodological flaws. I do not believe these points require further rebuttal or revision beyond what the authors have already provided.

In summary, in my view, the manuscript represents a solid contribution to the field, provided that the authors undertake a limited set of targeted revisions aimed at improving framing, clarity, and engagement with the broader literature. Addressing these points will strengthen the manuscript and ensure that its contributions are clearly and fairly communicated to the community.

Author response:

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

It is important to make a few key points about our work. First, our paper is largely a computational biophysics paper, augmented by experimental results. Generally speaking, computational biophysics work intends to achieve one of two things (or both). One is to provide more molecular level insight into various behaviors of biomolecular systems that have not been (or cannot be) provided by qualitative experimental results alone. The second general goal of computational biophysics it to formulate new hypotheses to be tested subsequently by experiment. In our paper, we have achieved both of these goals and then confirmed the key computational results by experiment.

eLife Assessment

This study investigates how the HIV inhibitor lenacapavir influences capsid mechanics and interactions with the nuclear pore complex. It provides important insights into how drug-induced hyperstabilization of the viral shell can compromise its structural integrity during nuclear entry. While the modeling is technically sophisticated and the results are promising, some mechanistic interpretations rely on assumptions embedded in the simulations, leaving parts of the evidence incomplete.

Given our response below, regarding the rigor and “completeness” of our work, we do not feel that an editorial judgement of “leaving parts of the evidence incomplete” is justified.

We also note that another recent experimental paper has validated essentially every prediction made in our eLife paper: https://www.biorxiv.org/content/10.64898/2026.01.05.697065v1

We thus disagree that the evidence we have presented in our paper is incomplete.

Public Reviews:

Reviewer #1 (Public review):

The paper from Hudait and Voth details a number of coarse-grained simulations as well as some experiments focused on the stability of HIV capsids in the presence of the drug lenacapavir. The authors find that LEN hyperstabilizes the capsid, making it fragile and prone to breaking inside the nuclear pore complex.

I found the paper interesting. I have a few suggestions for clarification and/or improvement. 

(1) How directly comparable are the NPC-capsid and capsid-only simulations? A major result rests on the conclusion that the kinetics of rupture are faster inside the NPC, but are the numbers of LENs bound identical? Is the time really comparable, given that the simulations have different starting points? I'm not really doubting the result, but I think it could be made more rigorous/quantitative.

We note (also in the manuscript) that it is difficult to compare the timescales obtained from coarse-grained MD simulations and experiments (“real time”) given that, by design, the CG simulations are accelerated to greatly enhance sampling. However, we can qualitatively compare the timescales of different CG simulations (without directly comparing the corresponding experimental timescales).

We agree with the reviewer that the starting point of NPC-capsid and capsid-only simulations is different, as is the biological environment in which the rupture occurs. When analyzing the NPC-only and capsid-only simulations, what was striking to us was that at the NPC the capsid-LEN complex ruptures in a multicomponent environment, where several FG-NUPs compete to displace the LENs. It is well established in experiments that LEN has a detrimental effect on capsid integrity.

In Figure 2, we plot the number of LEN molecules as a function of CG simulation time. The initial capsid-LEN complex was equilibrated without NPC and then placed at the cytoplasmic end of the NPC for docking. The number of LEN molecules for the capsid-only simulations and the NPC-docked simulations is nearly identical, and an insignificant number of LEN molecules unbind at the NPC. Hence, we added the following clarification:

Page 10, paragraph 11

“Note that the number of LEN molecules bound to the capsid for the free capsid and NPCdocked capsids are nearly identical. Hence, the disparity in timescale of lattice rupture is not only because of the effect of LEN on capsid lattice properties.”

Is the time really comparable, given that the simulations have different starting points?

Yes, the CG timescales of both the NPC and freely diffusing capsid unbiased simulations are comparable, since they were done using identical simulation settings.

(2) Related to the above, it is stated on page 12 that, based on the estimated free-energy barrier, pentamer dissociation should occur in ~10 us of CG time. But certainly, the simulations cover at least this length of time?

Our implicit solvent CG MD simulations are designed to access timescales far beyond the capabilities of the fully atomistic simulations. We reiterate here that it is difficult to directly compare the timescales obtained from CG MD simulations and experiments.

As described in the text, there are 12 pentamers in the capsid (7 in the wide end and 5 in the narrow end). For the narrow end to rupture, all 5 pentamers should progressively dissociate. In our unbiased simulations (Fig. S5), in 25 us of CG time, we observe (partial) dissociation of one or two pentamers. Hence, our unbiased CG simulation timescales were not long enough to observe rupturing of the narrow end.

(3) At first, I was surprised that even in a CG simulation, LEN would spontaneously bind to the correct site. But if I read the SI correctly, LEN was parameterized specifically to bind to hexamers and not pentamers. This is fine, but I think it's worth describing in the main text.

We modified (see below) the main text to include the details.

Page 4, paragraph 1

“We model LEN and CA interactions such that LEN molecules can only bind to CA hexamers, and all interactions to CA pentamers are turned off, as in experiments, CA selectively associates with hexamers (25, 36).”

Reviewer #2 (Public review):

Here, Hudait et al. use CG modeling to investigate the mechanism by which Lenacapavir (LEN) treats HIV capsids that dock to the nuclear pore complex (NPC). However, the manuscript fails to present meaningful findings that were previously unreported in the literature and is thus of low impact. Many claims made in the manuscript are not substantiated by the presented data. Key mechanistic details that the work purports to reveal are artifacts of the parameterization choices or simulation/analysis design, with the simulations said to reveal details that they were specifically biased to reproduce. This makes the manuscript highly problematic, as its contributions to the literature would represent misconceptions based on oversights in modeling and thus mislead future readers. 

We strongly disagree with these statements, and they do not reflect the facts. We provide a rebuttal to these statements in the “Author Response” statements below.

(1) Considering the literature, it is unclear that the manuscript presents new scientific discoveries. The following are results from this paper that have been previously reported:

(a) LEN-bound capsid can dock to the nuclear pore (Figure 2; see e.g. 10.1016/j.cell.2024.12.008 or 10.1128/mbio.03613-24). 

(b) NUP98 interacts with the docked capsid (Figure 2; see e.g. 10.1016/j.virol.2013.02.008 or 10.1038/s41586-023-06969-7 or 10.1016/j.cell.2024.12.008). 

(c) LEN and NUP98 compete for a binding interface (Figure 2; see e.g. 10.1126/science.abb4808 or 10.1371/journal.ppat.1004459). 

(d) LEN creates capsid defects (Figure 3 and 5, see e.g. 10.1073/pnas.2420497122). 

(e) RNP can emerge from a damaged capsid (Figure 3 and 5; see e.g. 10.1073/pnas.2117781119 or 10.7554/eLife.64776). 

(f) LEN hyperstabilizes/reduces the elasticity of the capsid lattice (Figure 6; see e.g. 10.1371/journal.ppat.1012537). 

The goal of our simulations (in combination with experiments from the Pathak group) is to provide molecular-level insight into the sequence of events of NPC docking of capsid and the effect of LEN binding leading to sequential dissociation of pentamers and leading to rupturing of the narrow end of the cone-shaped capsid. We also compare the events leading to capsid rupture at the NPC with the same for a freely diffusing capsid, akin to that in cytoplasm. The reviewer should carefully read the abstract of our paper. In fact, the above are all papers that present qualitative experimental results that help validate our model, but they do not provide details on the molecule-scale events. For example, the paper (10.1073/pnas.2420497122 written by our coauthors in the Pathak group) is extensively used to compare the behavior of LEN-bound capsid in the cytoplasm.

(2) The mechanistic findings related to how these processes occur are problematic, either based on circular reasoning or unsubstantiated, based on the presented data. In some cases, features of parameterization and simulation/analysis design are erroneously interpreted as predictions by the CG models. 

We strongly disagree with this assessment. Our CG NPC model is largely a “bottomup” model derived from molecular scale interactions sampled in atomistic simulations (see our previous paper in PNAS https://doi.org/10.1073/pnas.2313737121). The reviewer appears to be ignorant of the “bottom-up” approach based on rigorous statistical mechanics to derive moleculescale model (please refer to a detailed review on bottom-up coarse-graining: J. Chem. Theory. Comput., 2022, 18. 5759-5791).

Using the “bottom-up” CG model of the NPC, we predicted several molecular-level details of capsid import and docking to the NPC. Our key predictions were that there is an intrinsic capsid lattice elasticity and also the pleomorphic nature of the NPC channel is key for successful capsid docking https://doi.org/10.1073/pnas.2313737121). Our computational predictions have benn, for example, validated in a recently published paper by an experimental group: Hou, Z., Shen, Y., Fronik, S. et al. HIV-1 nuclear import is selective and depends on both capsid elasticity and nuclear pore adaptability. Nat Microbiol 10, 1868–1885 (2025). https://doi.org/10.1038/s41564025-02054-z). Our work is an excellent example of how systematically derived “bottom-up” CG models can accurately predict molecular details of complex biological processes.

We have now added the following statement:

Page 3, Paragraph 1

“Importantly, the computational predictions of capsid docking to the NPC central channel have been recently validated in a HIV-1 core import at the NPC using cryo-ET (33), demonstrating how systematically derived “bottom-up” CG models can accurately predict molecular details of complex biomolecular processes.”

(a) Claim: LEN-bound capsids remain associated with the NPC after rupture. CG simulations did not reach the timescale needed to demonstrate continued association or failure to translocate, leaving the claim unsubstantiated.

The reviewer fails to recognize that the statement is based on the experimental results of LEN-bound capsid that remains bound to the NPC after rupture and fails to translocate to the nuclear side (from the Pathak group in the section “Ruptured LEN-viral complexes remain bound to the NPC”). The Reviewers’ comment is incorrect. 

(b) Claim: LEN contributes to loss of capsid elasticity. The authors do not measure elasticity here, only force constants of fluctuations between capsomers in freely diffusing capsids. Elasticity is defined as the ability of a material to undergo reversible deformation when subjected to stress. Other computational works that actually measure elasticity (e.g., 0.1371/journal.ppat.1012537) could represent a point of comparison but are not cited. The changes in force constants in the presence of LEN are shown in Figure 6C, but the text of the scale bar legend and units of k are not legible, so one cannot discern the magnitude or significance of the change.

The concept of elasticity can extend down to the mesoscopic scale. Many examples can be found in the large number of elastic network models (ENMs) of proteins published by many authors. The reviewer also fails to comprehend the meaning of the effective spring constants in the HeteroENM model and how they relate to the response of the capsid to stress (e.g., in the NPC). Note, in the NPC central channel, the capsid encounters several nucleoporins (including disordered FG Nucleoporins that not have specific interactions to rest of the proteins), and also a confined environment. This environment can exert inward stress to the capsid, which is also reflected in stress on the capsid lattice. Furthermore, the cited computational AFM studies are very far from a realistic in vivo or even in vitro set of conditions. In contrast, our study presents a realistic environment which the capsid will encounter in NPC, and then these predictions are validated by experimental results.

(c) Claim: Capsid defects are formed along striated patterns of capsid disorder. Data is not presented that correlates defects/cracks with striations. 

We presented the data of formation of striated patterns of lattice stress in the capsid that runs from capsid narrow end to the wide end in coarse-grained model (https://doi.org/10.1073/pnas.2313737121), and atomistic model (https://doi.org/10.1073/pnas.2117781119). Both of our papers are extensively cited in the current manuscript. Also, when the capsid is ruptured, one cannot visualize the striated patterns.

(d) Claim: Typically 1-2 LEN, but rarely 3 bind per capsid hexamer. The authors state: "The magnitude of the attractive interactions was adjusted to capture the substoichiometric binding of LEN to CA hexamers (Faysal et al., 2024). ... We simulated LEN binding to the capsid cone (in the absence of NPC), which resulted in a substoichiometric binding (~1.5 LEN per CA hexamer), consistent with experimental data (Singh et al., 2024)." This means LEN was specifically parameterized to reproduce the 1-2 binding ratio per hexamer apparent from experiments, so this was a parameterization choice, not a prediction by CG simulations as the authors erroneously claim: "This indicates that the probability of binding a third LEN molecule to a CA hexamer is impeded, likely due to steric effects that prevent the approach of an incoming molecule to a CA hexamer where 2 LEN molecules are already associated. ... Approximately 20% of CA hexamers remain unoccupied despite the availability of a large excess of unbound LEN molecules. This suggests a heterogeneity in the molecular environment of the capsid lattice for LEN binding." These statements represent gross over-interpretation of a bias deliberately introduced during parameterization, and the "finding" represents circular reasoning. Also, if "steric effects" play any role, the authors could analyze the model to characterize and report them rather than simply speculate.

Reviewer comment: “This means LEN was specifically parameterized to reproduce the 1-2 binding ratio per hexamer apparent from experiments, so this was a parameterization choice, not a prediction by CG simulations as the authors erroneously claim.” – This comment by reviewer is deeply flawed and we strongly disagree. In our CG model there is no restriction on the number of LEN molecules that can bind to a CA hexamer. We again restate that, the experimental results on LEN binding to CA hexamers and inability of LEN to bind to pentamers were used as no allatom (AA) forcefield yet exists.

The steric effect of the lack of third LEN binding to a hexamer is a likely hypothesis (which one is allowed to make). More importantly, an investigation of the steric effect of LEN binding to the CA hexamer is not the main goal of the manuscript.

(e) Claim: Competition between NUP98 and LEN regulates capsid docking. The authors state: "A fraction of LEN molecules bound at the narrow end dissociate to allow NUP98 binding to the capsid ... Therefore, LEN can inhibit the efficient binding of the viral cores to the NPC, resulting in an increased number of cores in the cytoplasm." Capsid docking occurs regardless of the presence of LEN, and appears to occur at the same rate as the LEN-free capsid presented in the authors' previous work (Hudait &Voth, 2024). The presented data simply show that there is a fluctuation of bound LEN, with about 10 fewer (<5%) bound at the end of the simulation than at the beginning, and the curve (Figure 2A) does not clearly correlate with increased NUP98 contact. In that case, no data is shown that connects LEN binding with the regulation of the docking process. Further, the two quoted statements contradict each other. The presented data appear to show that NUP outcompetes LEN binding, rather than LEN inhibiting NUP binding. The "Therefore" statement is an attempt to reconcile with experimental studies, but is not substantiated by the presented data.

We disagree with this spurious statement, and we see no real contradiction. We have now added a minor clarification that LEN can inhibit efficient capsid binding at significantly high concentration.

Page 6, Paragraph 1

“Therefore, at significantly high concentration LEN can inhibit the efficient binding of the viral cores to the NPC, resulting in an increased number of cores in the cytoplasm.”

(f) Claim: LEN binding leads to spontaneous dissociation of pentamers. The CG simulation trajectories show pentamer dissociation. However, it is quite difficult to believe that a pentamer in the wide end of the capsid would dissociate and diffuse 100 nm away before a hexamer in the narrow end (previously between two pentamers and now only partially coordinated, also in a highly curved environment, and further under the force of the extruding RNA) would dissociate, as in Figure 2B. A more plausible explanation could be force balance between pent-hex versus hex-hex contacts, an aspect of CG parameterization. No further modeling is presented to explain the release of pentamers, and changes in pent-hex stiffness are not apparent in the force constant fluctuation analysis in Figure 6C.

This is both a misrepresentation of the simulations and a failure to understand them (as well as the supporting experiments) on the part of the reviewer. In the presence of LEN, the hexameric lattice is hyperstabilized. In contrast, the pentamers are not. As a consequence, the pentamers are dissociated. The pentamers at the narrow end are dissociated first, due to high curvature. The reviewer, from a point of being uninformed, simply speculates on what they think should happen. Moreover, as emphasized earlier and which the reviewer fails to comprehend is that ours is a “bottom-up CG model” so it predicts, not builds in, these effects.

(g) Claim: WTMetaD simulations predict capsid rupture. The authors state: "In WTMetaD simulations, we used the mean coordination number (Figure S6) between CA proteins in pentamers and in hexamers as the reaction coordinate." This means that the coordination number, the number of pent-hex contacts, is the bias used to accelerate simulation sampling. Yet the authors then interpret a change in coordination number leading to capsid rupture as a discovery, representing a fundamental misuse of the WTMetaD method. Changes in coordination number cannot be claimed as an emergent property when they are in fact the applied bias, when the simulation forced them to sample such states. The bias must be orthogonal to the feature of interest for that feature to be discoverable. While the reported free energies are orthogonal to the reaction coordinate, the structural and stepwise-mechanism "findings" here represent circular reasoning.

Unfortunately, the reviewer appears to be quite uninformed on the WTMetaD method and what it does. The chosen collective variable (CV) in our case is the coordination variable and the MetaD samples along that variable (the conditional free energy) as it is designed to do. The reviewer may wish to educate themself by reading Dama et al (https://doi.org/10.1103/PhysRevLett.112.240602). We also note that “emergent properties” are not along some other, uncoupled coordinate.

(3) Another major concern with this work is the excessive self-citation, and the conspicuous lack of engagement with similar computational modeling studies that investigate the HIV capsid and its interactions with LEN, capsid mechanical properties relevant to nuclear entry, and other capsidNPC simulations (e.g., 10.1016/j.cell.2024.12.008 and 10.1371/journal.ppat.1012537). Other such studies available in the literature include examination of varying aspects of the system at both CG and all-atom levels of resolution, which could be highly complementary to the present work and, in many cases, lend support to the authors' claims rather than detract from them. The choice to omit relevant literature implies either a lack of perspective or a lack of collegiality, which the presentation of the work suffers from. Overall, it is essential to discuss findings in the context of competing studies to give readers an accurate view of the state of the field and how the present work fits into it. It is appropriate in a CG modeling study to discuss the potential weaknesses of the methodology, points of disagreement with alternative modeling studies, and any lack of correlation with a broader range of experimental work. Qualitative agreement with select experiments does not constitute model validation. 

We disagree with this statement and point out where we have cited other work, including the ones mentioned above. However, our CG model is a largely bottom-up CG model which differs from other more ad hoc CG approaches (and some well-known CG models). We do not wish to emphasize the obvious flaws in those other CG approaches and models, since that is not the focus of our manuscript.

(4) Other critiques, questions, concerns:

(a) The first Results sub-heading presents "results", complete with several supplementary figures and a movie that are from a previous publication about the development of the HIV capsid-NPC model in the absence of LEN (Hudait &Voth, 2024). This information should be included as part of the introduction or an abbreviated main-text methods section rather than being included within Results as if it represents a newly reported advancement, as this could be misleading. 

The movie in question (capsid docking to NPC without LEN) is essential for comparison of LEN-binding dynamics. Different from our previous paper, we simulated significantly longer timescales of capsid docking and performed several additional analyses that is relevant to this paper. Moreover, the first section of the result is titled “Coarse-grained modeling and simulation”, hence we only present a summary of the CG models and key validation steps in this section.

(b) The authors say the unbiased simulations of capsid-NPC docking were run as two independent replicates, but results from only one trajectory are ever shown plotted over time. It is not mentioned if the time series data are averaged or smoothed, so what is the shadow in these plots (e.g., Figures 1,2, and Supplementary Figure 5)?

These simulations are the average from two replicas. “For all the plots, the solid lines are the mean values calculated from the time series of two independent replicas, and the shaded region is the standard deviation at each timestep.” This was mentioned in the original figure caption.

(c) Why do the insets showing LEN binding in Figure 2A look so different from the models they are apparently zoomed in on? Both instances really look like they are taken from different simulation frames, rather than being a zoomed-in view.

It is difficult to discern a high curvature region of the capsid due to object overlap of different regions of the capsid. This is likely a case of “perspective distortion” in image processing.

(d) What are the sudden jerks apparent in the SI movies? Perhaps this is related to the rate at which trajectory frames are saved, but occasionally, during the relatively smooth motion of the capsidNPC complex, something dramatic happens all of a sudden in a frame. For example, significant and apparently instantaneous reorientation of the cone far beyond what preceding motions suggest is possible (SI movie 2, at timestamp 0.22), RNP extrusion suddenly in a single frame (SI movie 2, at timestamp 0.27), and simultaneous opening of all pentamers all at once starting in a single frame (SI movie 2, at timestamp 0.33). This almost makes the movie look generated from separate trajectories or discontinuous portions of the same trajectory. If movies have been edited for visual clarity (e.g., to skip over time when "nothing" is happening and focus on the exciting aspects), then the authors should state so in the captions. 

This is due to the rate at which trajectory frames are saved for movie generation for faster processing of the movies. We added the following in movie caption: 

“The movie frames correspond to snapshots every 250000 𝜏_CG.” 

(e) Figure 3c presents a time series of the degree of defects at pent-hex and hex-hex interfaces, but I do not understand the normalization. The authors state, "we represented the defects as the number of under-coordinated CA monomers of the hexamers at the pentamer-hexamer-pentamer and hexamer-hexamer interface as N_Pen-Hex and N_Hex-Hex ... Note that in N_Pen-Hex and N_Hex-Hex are calculated by normalizing by the total number of CA pentamer (12) and hexamer rings (209) respectively." Shouldn't the number of uncoordinated monomers be normalized by the number of that type of monomer, rather than the number of capsomers/rings? E.g., 12*5 and 209*6, rather than 12 and 209?

We prefer to continue with the current normalization, since typically in the HIV-1 literature capsids are represented as a collection of hexamers and pentamers (rather than total number of CA monomers).

(f) The authors state that "Although high computational cost precluded us from continuing these CG MD simulations, we expect these defects at the hexamer-hexamer interface to propagate the high curvature ends of the capsid." The defects being reported are apparently propagating from (not towards) the high curvature ends of the capsid. 

We corrected the statement as follows:

“Although high computational cost precluded us from continuing these CG MD simulations, we expect these defects at the hexamer-hexamer interface to propagate from the high curvature to low curvature end of the capsid.”

(g) The first half of the paper uses the color orange in figures to indicate LEN, but the second half uses orange to indicate defects, and this could be confusing for some readers. Both LEN and "defects" are simply a cluster of spheres, so highlighted defects appear to represent LEN without careful reading of captions.

We only show LEN in Figure 1, and in rest of the figures the bound LEN molecules are not shown for clarity. The defects are shown in a darker shade of orange (amber). 

(h) SI Figure S3 captions says "The CA monomers to which at least one LEN molecule is bound are shown in orange spheres. The CA monomers to which no LEN molecule is bound are shown in white spheres. " While in contradiction, the main-text Fig 2 says "The CA monomers to which at least one LEN molecule is bound are shown in white spheres. The CA monomers to which no LEN molecule is bound are shown in orange spheres. " One of these must be a typo.

We have corrected the erroneous caption in Fig. S3. The color scheme in Fig. 2 and Fig. S3 are now consistent.

(i) The authors state that: "CG MD simulations and live-cell imaging demonstrate that LEN-treated capsids dock at the NPC and rupture at the narrow end when bound to the central channel and then remain associated to the NPC after rupture." However, the live cell imaging data do not show where rupture occurs, such that this statement is at least partially false. It is also unclear that CG simulations show that cores remain bound following rupture, given that simulations were not extended to the timescale needed to observe this, again rendering the statement partially false.

We modified the statement as follows:

“CG MD simulations complemented by the outcome of live-cell imaging demonstrate that LENtreated capsids dock at the NPC and rupture at the narrow end when bound to the central channel and then remain associated with the NPC after rupture.”

(j) The authors state: "We previously demonstrated that the RNP complex inside the capsid contributes to internal mechanical strain on the lattice driven by CACTD-RNP interactions and condensation state of RNP complex (Hudait &Voth, 2024). " In that case, why do the present CG models detect no difference in results for condensed versus uncondensed RNP?

In our previous paper, the difference from condensation state of RNP complex appear only in the pill-shaped capsid, and not in the cone-shaped capsid. In this manuscript, we only investigated the cone-shaped capsid.

(k) The authors state: "The distribution demonstrates that the binding of LEN to the distorted lattice sites is energetically favorable. Since LEN localizes at the hydrophobic pocket between two adjoining CA monomers, it is sterically favorable to accommodate the incoming molecule at a distorted lattice site. This can be attributed to the higher available void volume at the distorted lattice relative to an ordered lattice, the latter being tightly packed. This also allows the drug molecule to avoid the multitude of unfavorable CA-LEN interactions and establish the energetically favorable interactions leading to a successful binding event. " What multitude of unfavorable interactions are the authors referring to? Data is not presented to substantiate the claim of increased void volume between hexamers in the distorted lattice. Capsomer distortion is shown as a schematic in Figure 6A rather than in the context of the actual model.

“What multitude of unfavorable interactions are the authors referring to?” We have now added the following sentence to clarify

“Here we denote unfavorable CA-LEN interactions as all interactions other than the electrostatic and van der Waal interactions that lead to CA-LEN binding (17).”

“In the distorted lattice, there is an increase of void volume is based on standard solid-state physics understanding. We added the word “likely” in the statement. “. This can likely be attributed to the higher available void volume at the distorted lattice relative to an ordered lattice, the latter being tightly packed (41).”

Moreover, in one of our previous manuscripts, we established that compressive or expansive strain induces more closely packed or expanded lattice (A. Yu et al., Strain and rupture of HIV-1 capsids during uncoating. Proceedings of the National Academy of Sciences 119, e2117781119 (2022)).

(l) The authors state that "These striated patterns also demonstrate deviations from ideal lattice packing. " What does ideal lattice packing mean in this context, where hexamers are in numerous unique environments in terms of curvature? What is the structural reference point?

The ideal lattice packing definition is provided in our previous manuscripts: 1. A. Yu et al., Strain and rupture of HIV-1 capsids during uncoating. Proceedings of the National Academy of Sciences 119, e2117781119 (2022), 2. A. Hudait, G. A. Voth, HIV-1 capsid shape, orientation, and entropic elasticity regulate translocation into the nuclear pore complex. Proceedings of the National Academy of Sciences 121, e2313737121 (2024).

These manuscripts are cited in the previous statement. The ideal lattice packing is defined based on lattice separations in each core (in cryo-ET and atomistic simulations) using a local order parameter, which measures the near-neighbor contacts of a particle. Moreover, the ideal packing reference is calculated from all available capsid shapes (cone, ellipsoid, and tubular), and takes into account different curvatures.

(m) If pentamer-hexamer interactions are weakened in the presence of LEN, why are differences at these interfaces not apparent in the Figure 6C data that shows stiffening of the interactions between capsomer subunits?

We have added a statement as follows:

“Based on our analysis, we hypothesize that LEN binding hyperstabilzes the CA hexamerhexamer interactions relative to CA hexamer-pentamer interaction.”

(n) The authors state: "Lattice defects arising from the loss of pentamers and cracks along the weak points of the hexameric lattice drive the uncoating of the capsid." The word rupture or failure should be used here rather than uncoating; it is unclear that the authors are studying the true process of uncoating and whether the defects induced by LEN binding relate in any way to uncoating. 

We have now changed “uncoating” to “rupture” throughout the manuscript.

(o) The authors state: " LEN-treated broken cores are stabilized by the interaction with the disordered FG-NUP98 mesh at the NPC." But no data is presented to demonstrate that capsid stability is increased by NUP98 interaction. In fact, the presented data could suggest the opposite since capsids in contact with NUP98 in the NPC appeared to rupture faster than freely diffusing capsids.

We have modified the statement as follows

“We hypothesize that LEN-treated broken cores are stabilized by the interaction with the disordered FG-NUP98 mesh at the NPC.”

(p) The authors state: "LEN binding stimulates similar changes in free capsids, but they occur with lower frequency on similar time scales, suggesting that the cores docked at the NPC are under increased stress, resulting in more frequent weakening of the hexamer-pentamer and hexamerhexamer interactions, as well as more nucleation of defects at the hexamer-hexamer Interface. ... Our results suggest that in the presence of the LEN, capsid docking into the NPC central channel will increase stress, resulting in more frequent breaks in the capsid lattice compared to free capsids." The first is a run-on sentence. The results shown support that LEN stimulates changes in free capsids to happen faster, but not more frequently. The frequency with which an event occurs is separate from the speed with which the event occurs.

We have fixed the run-on sentence.

The results shown support that LEN stimulates changes in free capsids to happen faster, but not more frequently. The frequency with which an event occurs is separate from the speed with which the event occurs.

We disagree with the reviewer. The statement was intended to provide a comparison between free capsid and NPC-bound capsid.

(q) The authors state: "A possible mechanistic pathway of capsid disassembly can be that multiple pentamers are dissociated from the capsid sequentially, and the remaining hexameric lattice remains stabilized by bound LEN molecules for a time, before the structural integrity of the remaining lattice is compromised." This statement is inconsistent with experimental studies that say LEN does not lead to capsid disassembly, and may even prevent disassembly as part of its disruption of proper uncoating (e.g., 10.1073/pnas.2420497122 previously published by the authors).

We disagree with the interpretation of the reviewer. Our interpretation based on our results is LEN binding accelerates capsid rupture (from pentamer-rich high curvature ends), and the rest of the broken hexameric lattice is hyperstabilized. Ultimately, lattice rupture will lead to release the RNP, and hence the intended goal of the drug is achieved.

(r) Finally, it remains a concern with the authors' work that the bottom-up solvent-free CG modeling software used in this and supporting works is not open source or even available to other researchers like other commonly used molecular dynamics software packages, raising significant questions about transparency and reproducibility.

The simulations were performed in LAMMPS, which is open source. This software is already stated in the Methods. Input data is provided upon request.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 1: In part B, it appears the middle panel was screenshotted from a ppt, given the red line underneath Lenacapavir. You can export it to an image instead.

The figure is fixed.

(2) Figure 6: In part A, the LEN_d in the graph is illegible. Also, in the panel next to it, it also appears to have been screenshotted from a ppt.

The figure is fixed.

(3) Page 6: There's an errant quotation mark at the end of a paragraph.

Removed the errant quotation

Reviewer #2 (Recommendations for the authors):

The code used to perform bottom-up solvent-free CG modeling simulations is not made available.

This is not true. LAMMPS was used as stated in Methods.

eLife Assessment

In this fundamental work Horne et al present compelling evidence that YbjP is a novel binding partner of the TolC channel protein. The YbjP is characterized using cryo-EM, and its role probed using pull-down experiments, in vivo crosslinking, functional assays along with phylogenetic analysis which are all properly performed and presented and support the main conclusions. While the study does not identify a clear role for this protein, the revised manuscript offers improved clarity and contributes invaluable insight into membrane transport and antimicrobial resistance.

Reviewer #2 (Public review):

This article focuses on the study of two E. coli tripartite efflux pumps, both using TolC as a partner in the outer membrane, namely MacAB-TolC and AcrABZ-TolC.

By preparing MacAB-TolC in Peptidiscs rather than in detergent for cryo-EM structure determination, they visualized an extra protein localized around TolC. The resolution was sufficient to build part of the structure, and using the AlphaFold2 database and DALI topology recognition program, they identified it as the lipoprotein YbjP. This protein has an anchorage in the outer membrane, and it was suggested that it could act as a support for TolC, which is the only OMF that does not have an N-terminal extension anchored in the outer membrane, which is very puzzling for the community working in this field of research.

Authors used a large number of different approaches to evaluate the importance of YbjP (structure, genomic evolution, microbiology, photocrosslink in vivo, proteomic profile), but did not succeed in finding it a clear role so far, even if it could be important depending on environmental stress. Nevertheless, their results, obtained with extreme rigour, are of main interest for the comprehension of the complexity of such systems and deserve publication.

Comments on revisions:

Thank you for clarifying the points that puzzled me concerning the crosslink experiments. This version does not need further modifications.

Author Response:

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

Reviewer #1 (Public review):

The presentation and especially main-text illustrative material seem to focus disproportionately on MacAB-TolC-YbjP complex, and the AcrABZ-TolC-YbjP is relegated to supplementary data which is somewhat confusing. There is no high-resolution side view of the AcrABZ-TolC-YbjP side-by-side to MacAB-TolC-YbjP which may be helpful to spot parallels and differences in the organisation of the two systems.

This was previously presented in Supplementary Figure S2. However, because the models were shown at a small scale, we have now included the comparison in a main manuscript (Figure 4). This figure presents AcrABZ-TolC-YbjP and MacAB-TolC-YbjP side-by-side, a structural alignment of TolC-YbjP in the two pumps, and close-up views of the interaction interface.

Supplementary Figure 2 may also be better presented in the main text, as it shows specific displacements of residues upon binding of the YbjP relative to the apo-complexes, although this can be left at the authors' discretion.

We added more text to describe the displacements of residues upon YbjP binding: ‘Nonetheless, the side chains of a few residues in TolC, which mainly correspond to positively charged amino acids (R18, R24, K214, R227, R234), reorient to interact with the YbjP lipoprotein partner (Figure 2B).’

Reviewer #1 (Recommendations for the authors):

The work is of high quality and requires minimal modifications, which are mentioned as suggestions above and are mostly connected to the illustrative material.

One additional suggestion, which is connected to the earlier BioRxiv preprint, the data seen in Fig 6 of the preprint seems to have been edited out from the current version, and perhaps can be included in a revised version, as it seems to support the "rapid adaptation under stress" role for YbjP, which currently is only speculatively mentioned in p.11, line 365 of the manuscript.

We acknowledge that the BioRxiv preprint Figure 6 can support the rapid adaptation under stress role for YbjP. However, upon sequencing the ΔybjP strain from the Keio collection used in the preprint, we identified a large deletion in the yecT-flhD region. We therefore generated a new ΔybjP strain without the yecT-flhD deletion and repeated the experiment. However, the results with the corrected strain did not support the previous conclusion, and these data were consequently removed in the current manuscript.

Reviewer #2 (Public review):

In Figure 3C, the experiment performed with AcrA is clear and the extra band appears at the proper size. On the right panel, it is clear that the crosslink doesn't work when pBPA is placed on residues too far from TolC. Only when introduced on N113 or T110 does a band appear.

This is in accordance with an interaction in vivo. Nevertheless, 17 + 54 = 71kDa, which is more than the two bands appearing on the gel. This difference in size migration can occur, but it is not clear when looking at Figure S3. In Figure S3a, the purified proteins are highlighted at approximately the expected size (≈20kDa instead of 17 for YbjP and between 56 and 60kDa in two bands for TolC instead of 54kDa). On the right panel, it seems that the bands are present exactly at the same position, instead of an upper band as expected for the crosslinked YbjP-TolC (at 71kDa). It would be clearer if having the control of the same sample without illumination, revealed by anti-TolC, to see the difference.

We thank the reviewer for pointing out this discrepancy. We identified an error in the molecular weight ladder, as one band was missing. This has now been corrected: YbjP migrates just below 17 kDa, consistent with Figure 3C. In addition, we previously reported a size of 54 kDa for TolC, whereas matured TolC, after signal peptide cleavage, is actually 52 kDa.

We believe that the differences in the apparent molecular weight observed in Figures 3A, 3C and S3 (now S2) mainly result from tagging and post-translation modifications.

In Figure 3A, we used the soluble construct His-YbjP_28-1711 (theoretical M_w ~18 kDa), as also done for the controls in Figures 3C and S3 (now S2). However, for the crosslinking samples, we used full-length His-tagged YbjP, which carries a post-translational lipid modification (theoretical M_w ~19 kDa, considering the protein lipidation). The presence of the lipid chains alters the migration as this species migrates at ~15 kDa (Fig 3A). Increased hydrophobicity, due here to YbjP lipidation, could accelerate the migration (Emmanuel et al. 2025 FEBS Open Bio).

In Figure 3A, we used the TolC-FLAG whose apparent M_w is ~52 kDa, as previously reported (Fig S3, Fitzpatrick et al. 2017). In Figure S3 (now S2), we used His-tagged TolC (theoretical M_w 55 kDa) for the control, which migrates above 56 kDa. In the crosslinking samples, however, we detect tag-free, endogenous TolC, with a theoretical M_w of ~51 kDa.

In conclusion, the crosslinked complex composed of lipidated FL YbjP (~15 kDa) and endogenous TolC (~51 kDa) would be expected to migrate at ~66 kDa, which is consistent with what is observed in Figures 3C and S3 (now S2).

A second point that could be discussed further is the comparison of the structure of the pump in the presence of the peptidoglycan with the images previously obtained by tomography. It is not totally clear to me if YbjP could have been positioned in these maps.

There is density corresponding to YbjP in the map obtained in the presence of peptidoglycan. To improve clarity, we have specified the location of the peptidoglycan relative to the pumps in the revised Figure 4, and Supplementary Figure S4, together with the position of YbjP. In both figures, the lipoprotein appears distant from the peptidoglycan density.

Reviewer #2 (Recommendations for the authors):

In addition, please add explanations in the legend of Figure 3C concerning the structures.

We added the following description of the structures: ‘As shown underneath, AcrA residues Q136 and Y137, proximal to TolC in the structure of the AcrABZ-TolC pump (PDB 5NG5), were replaced by pBPA. For YbjP, the two residues N113 and T110 proximal to TolC in the MacAB-TolC-YbjP complex (PDB 9QGY) and the three residues N43, N90 and H104 distal to TolC were mutated.’

It would be clearer if having the control of the same sample without illumination, revealed by anti-TolC, to see the difference.

As the amount of crosslinked material is low, samples were enriched via His-tag purification of YbjP prior to Western blotting. In the absence of illumination (see sample N113, UV-), no crosslink would be formed, and therefore TolC would not be co-purified.

In addition, some typo errors have been noted.

Table S1 minus is missing for the defocus range for AcrABZ-TolC-YbjP.

Thank you for noting the typo. We have added the minus sign.

Table S3, please specify what is N in the legend.

N is the stoichiometry parameter, which is now specified in the table legend.

Line 237, I suppose it has to refer to Figure S6, not S5.

Thank you for noting the error. We have verified the text matches the figures here and in the entire manuscript.

Several errors are present in the legend of Figure 6.

No letters are indicated for the different panels; line 841 must be C, F and I; the indicated colors for the differentially expressed proteins do not correspond to the volcano plots.

Thank you for suggesting the improvements for the labels. We have modified the plot accordingly.

Reference Glavier 2020 has been cited as Glacier on line 72.

We have modified the writing accordingly and checked the reference.

eLife Assessment

This is an important study that takes a key step towards understanding developmental disorders linked to mutations in the O-GlcNAc transferase enzyme by generating a mouse model harboring the C921Y mutation. While the mechanisms remain open, the study thoroughly examines behavioral and anatomical differences in these mice and provides convincing evidence for behavioral hyperactivity and learning/memory deficits, as well as phenotypic differences in skull and brain formation. This study will be of interest to those studying neurodevelopmental disorders and associated mechanisms.

Reviewer #1 (Public review):

This study established a C921Y OGT-ID mouse model, systematically demonstrating in mammals the pathological link between O-GlcNAc metabolic imbalance and neurodevelopmental disorders (cortical malformation, microcephaly) as well as behavioral abnormalities (hyperactivity, impulsivity, learning/memory deficits). Researchers comprehensively assessed the model phenotype through integrated multi-level analysis methods, including long-term behavioral monitoring, high-resolution brain structural imaging (micro-CT and MRI), histopathology, and quantitative proteomics.

The core strength of this study lies in its multimodal experimental design. The evidence chain spanning in vivo behavior, brain structure, and molecular characteristics demonstrates high consistency and correlation. Of particular note is the combination of non-invasive behavioral tracking with quantitative neuroimaging techniques, providing objective validation for the observed phenotypes. The findings support the authors' core conclusion: O-GlcNAc homeostasis imbalance correlates with neurodevelopmental deficits, including structural abnormalities in specific brain regions and altered cognitive behaviors. Furthermore, this model reproduces certain clinical features observed in human patients.

Nevertheless, several avenues remain open for further exploration. For instance, sample sizes in certain omics analyses remain relatively small, and investigations into downstream molecular mechanisms are still confined to the level of correlation-direct causal validation through genetic or pharmacological interventions is still required. Furthermore, as this model focuses on a single recurrent mutation, the generalizability of its findings to other OGT-ID variants remains to be verified.

It provides the first actionable vertebrate model for neurodevelopmental disorders with unclear mechanisms, filling a critical gap in this field. The multidimensional research methods established in the paper-such as the digital behavioral phenotyping workflow-also offer valuable references for related disease studies.

Reviewer #2 (Public review):

Summary:

The authors are trying to understand why certain mutants of O-GlcNAc transferase (OGT) appear to cause developmental disorders in humans. As an important step towards that goal, the authors generated a mouse model with one of these mutations that disrupts OGT activity. They then go on to test these mice for behavioral differences, finding that the mutant mice exhibit some signs of hyperactivity and differences in learning and memory. They then examine alterations to the structure of the brain and skull, and again find changes in the mutant mice that have been associated with developmental disorders. Finally, they identify proteins that are up or down regulated between the two mice as potential mechanisms to explain the observations.

Strengths:

The major strength of this manuscript is the creation of this mouse model, as a key step in beginning to understand how OGT mutants cause developmental disorders. This line will prove important for not only the authors but other investigators as well, enabling the testing of various hypotheses and potentially treatments. The experiments are also rigorously performed and the conclusions are well supported by the data.

Weaknesses:

The only weakness is a lack of mechanistic insight. However, this certainly may come in the future through more targeted experimentation using this mouse model. I do not recommend that these experiments need to be performed in this manuscript.

Comments on revisions:

The authors have addressed all of my suggestions proactively.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

This study established a C921Y OGT-ID mouse model, systematically demonstrating in mammals the pathological link between O-GlcNAc metabolic imbalance and neurodevelopmental disorders (cortical malformation, microcephaly) as well as behavioral abnormalities (hyperactivity, impulsivity, learning/memory deficits). However, critical flaws in the current findings require resolution to ensure scientific rigor.

The most concerning finding appears in Figure S12. While Supplementary Figure S12 demonstrates decreased OGA expression without significant OGT level changes in C921Y mutants via Western blot/qPCR, previous reports (Florence Authier, et al., Dis Model Mech. 2023) described OGT downregulation in Western blot and an increase in qPCR in the same models. The opposite OGT expression outcomes in supposedly identical mouse models directly challenge the model's reliability. This discrepancy raises serious concerns about either the experimental execution or the interpretation of results. The authors must revalidate the data with rigorous controls or provide a molecular biology-based explanation.

We thank the reviewer for their time and effort in improving the quality of our manuscript.

We would like to point out that the results presented in the previous Fig. S12 (now Fig. S13) are from different ages of the mice and restricted to the prefrontal cortex, compared to the previous report (Florence Authier, et al., Dis Model Mech. 2023) where we showed OGT and OGA mRNA/protein expression in total brain homogenates. In this previous study, we observed a significant reduction in OGT protein levels while OGT mRNA levels were significantly increased in the brains of 3 months old mutant C921Y compared to WT controls. However, in our current study (Figure S12, now S13), OGA and OGT mRNA/protein expression have been a) restricted to the pre-frontal cortex and b) are from 4 months old male mice. Therefore, a direct comparison of findings from total brain vs. prefrontal cortex would be speculative. In our present work, OGT protein levels are not changed in the pre-frontal cortex, while OGT mRNA levels are increased (similarly to the total brain data), albeit not significantly.

It is plausible that the different levels of OGT protein expression in total brain (previous study) and prefrontal cortex (current study) potentially reflect regional differences in the regulation of OGT protein levels/stability, since OGT mRNA levels are increased in both cases. This notion is also supported by additional analyses in three other brain regions (hippocampus, striatum and cerebellum) and these data are now included in Figures S13 and S14.

A few additional comments to the author may be helpful to improve the study.

Major

(1) While this study systematically validated multi-dimensional phenotypes (including neuroanatomical abnormalities and behavioral deficits) in OGT C921Y mutant mice, there is a lack of relevant mechanisms and intervention experiments. For example, the absence of targeted intervention studies on key signaling pathways prevents verification of whether proteomics-identified molecular changes directly drive phenotypic manifestations.

We agree with the reviewer that the suggested experiments would further strengthen our work. However, the extensive nature of the suggested studies would result in considerable delay in sharing this work with the scientific and patient communities. Nevertheless, we appreciate the reviewers’ comment and will continue to work along these lines, and report in a follow up manuscript in the future.

(2) Although MRI detected nodular dysplasia and heterotopia in the cingulate cortex, the cellular basis remains undefined. Spatiotemporal immunofluorescence analysis using neuronal (NeuN), astrocytic (GFAP), and synaptic (Synaptophysin) markers is recommended to identify affected cell populations (e.g., radial glial migration defects or intermediate progenitor differentiation abnormalities).

Following the reviewers’ suggestion, we have performed additional analyses to identify the cellular composition of the observed nodular dysplasia using neuronal and glial markers. These new analyses indicate that the nodular collections in the layers II/III were predominantly neurons, for example see cresyl violet (Fig. 6E). Moreover, we have also performed immunofluorescence imaging using NeuN and GFAP (Fig. 6G-H), which reflect that the dystrophic collections are predominantly neurons. To further corroborate these findings, we have also performed multiplex IHC analyses, presented in Fig. S12, which indicate that: i) the nodular cortical malformations were populated by neurons and oligodendrocytes and ii) predominantly affected layers II-V, as reflected by the distribution of neuronal markers Reelin and POU class 3 homeobox 2 (POU3F2), and collectively (Fig. 6 and Fig. S12) reflect neuronal disorganisation due to migration defects rather than differentiation defects. We appreciate the reviewers’ suggestion to perform spatiotemporal analyses of these cellular features; however, tissue from defined stages of development is not available. 

(3) While proteomics revealed dysregulation in pathways including Wnt/β-catenin and mTOR signaling, two critical issues remain unresolved: a) O-GlcNAc glycoproteomic alterations remain unexamined; b) The causal relationship between pathway changes and O-GlcNAc imbalance lacks validation. It is recommended to use co-immunoprecipitation or glycosylation sequencing to confirm whether the relevant proteins undergo O-GlcNAc modification changes, identify specific modification sites, and verify their interactions with OGT.

We agree with the referee that these experiments would further strenghten the work. However, we respectfully point out that the inference that altered proteins must themselves be O-GlcNAc modified is not necessarily correct. For instance, O-GlcNAcylation of unknown protein kinase X, E3 ligase/DUB, Y or transcription factor Z could indirectly affect these pathways/proteins. Nevertheless, we have performed further experiments to explore whether Wnt/β-catenin and mTOR signalling are functionally affected, as pointed out by the referee. In the qPCR analyses, we did not observe significant changes in expression of Wnt target genes (Cdkn1a, Ccnd1, Myc, Ramp3, Tfrc), neither in protein levels of key proteins involved in Wnt/β-catenin (non-phosphorylated β-catenin) and mTOR (phosphorylated rpS6) signalling by western blots (data not shown). These results suggest that both pathways are not functionally deregulated in prefrontal cortex of adult OGT^C921Y mice to a significant extent.

(4) Given that OGT-ID neuropathology likely originates embryonically, we recommend serial analyses from E14.5 to P7 to examine cellular dynamics during critical corticogenesis phases.

We appreciate the reviewers’ suggestion to perform spatiotemporal analyses of these cellular dynamics; however, tissue from defined stages of development is not available. As stated above, we want to share our current findings with the scientific and patient communities in a timely manner, and the suggested experiments could form the foundation of a follow up study in the future.

(5) The interpretation of Figure 8A constitutes overinterpretation. Current data fail to conclusively demonstrate impairment of OGT's protein interaction network and lack direct evidence supporting the proposed mechanisms of HCF1 misprocessing or OGA loss.

Thank you for the comment. To avoid misleading the readers, we have removed panel A from the previous version of Figure 8 and updated the version of record.

Reviewer #2 (Public review):

Summary:

The authors are trying to understand why certain mutants of O-GlcNAc transferase (OGT) appear to cause developmental disorders in humans. As an important step towards that goal, the authors generated a mouse model with one of these mutations that disrupts OGT activity. They then go on to test these mice for behavioral differences, finding that the mutant mice exhibit some signs of hyperactivity and differences in learning and memory. They then examine alterations to the structure of the brain and skull and again find changes in the mutant mice that have been associated with developmental disorders. Finally, they identify proteins that are up- or down-regulated between the two mice as potential mechanisms to explain the observations.

Strengths:

The major strength of this manuscript is the creation of this mouse model, as a key step in beginning to understand how OGT mutants cause developmental disorders. This line will prove important for not only the authors but other investigators as well, enabling the testing of various hypotheses and potentially treatments. The experiments are also rigorously performed, and the conclusions are well supported by the data.

Weaknesses:

The only weakness identified is a lack of mechanistic insight. However, this certainly may come in the future through more targeted experimentation using this mouse model.

We agree with the reviewer that the suggested experiments would further strengthen our work. However, the extensive nature of the suggested studies would result in considerable delay in sharing this work with the scientific and patient communities. Nevertheless, we appreciate the reviewers’ comment and will continue to work along these lines, and report in a follow up manuscript in the future.

Recommendations for the authors:

Editor's note:

Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and, where appropriate, 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

Statistics including exact p-values have been included in the main text for all key questions where appropriate.

Reviewer #1 (Recommendations for the authors):

(1) In Figure 1F, the y-axis labels and scale values are partially obscured by graphical elements, compromising accurate interpretation of the data range.

Panel 1F has been adjusted to make the y-axis label visible.

(2) Regarding the histological analyses in Figure 6, the current H&E staining and Luxol Fast Blue myelin staining results lack age-matched wild-type control samples processed in parallel, which undermines experimental comparability. To enhance methodological rigor, control group staining results should be displayed adjacent to each experimental group image.

The original Figure 6 already contained comparison between WT and OGT^C921Y tissues. The Figure has been updated with additional data from the WT and C921Y mutant groups shown side by side.

Reviewer #2 (Recommendations for the authors):

(1) I believe that Figures S1 and S2 were switched during the submission. The legends are correct, so the authors should just be careful with the order when they upload the final versions.

Figures S1 and S2 have been re-ordered.

(2) On page 18, the authors state, "Although no significant changes in the expression of OGT were observed in OGTC921Y cortex (Figure S12A, C), there was a significant increase in OGT/OGA protein ratio in OGTC921Y mice (Fig. S12D). As a functional consequence, global O-GlcNAcylation of proteins in the brain was drastically impaired in the OGTC921Y brain compared to WT (Figure S12E, F).

To me, this statement suggests that the incorrect ratio of OGT to OGA is responsible for the altered O-GlcNAc levels. I think this is missing important information. The authors are, I'm sure, aware that OGT and OGA expression is linked to O-GlcNAc levels. I think it would be better to describe the situation here as the tissue attempting to respond to lower OGT activity by lowering OGA levels. However, the tissue is not fully successful, resulting in lower overall O-GlcNAc levels as seen by RL2. If the difference were only driven by the OGT/OGA ratio, one would expect increased O-GlcNAc levels due to decreased OGA. I think it is important to point out more details here for non-expert readers.

Thank you for the insightful comment, we have included these aspects in the revised text, please see page 20.

(3) I am a little surprised that the authors did not explore differences in O-GlcNAc-modified proteins through a more targeted enrichment of these proteins for analysis of potential modification differences, in addition to just changes in protein abundance.

We agree that these experiments would further strengthen the work. However, it is not known yet whether OGT-CDG is caused by loss of O-GlcNAc modification on specific proteins or due to as yet to decipher mechanisms (e.g. OGT interactome, HCF1 processing, feedback on OGA levels) which we are not able to confirm in the current manuscript. Therefore, as a starting point, we have performed whole proteome analysis to establish candidate hypothesis which could lead to discovering cellular and molecular mechanisms underlying OGT-CDG. Lastly, we appreciate the reviewers’ comment and will continue to work along these lines, and report in a follow up manuscript in the future.

eLife Assessment

This important study presents a compelling link between nutrient signaling and chromosome regulation, demonstrating that reduced activity in a central nutrient-sensing pathway improves chromosome stability and alters gene expression through effects on cohesin. The convincing evidence from a combination of genetic, biochemical and cell biological approaches supports a model in which TORC1-dependent phosphorylation of Mis4 and the cohesin subunit Psm1/Smc1 can modulate cohesin loading to enhance faithful chromosome transmission. While the underlying mechanisms and biological importance of this newly described circuit are not yet fully known, the overall body of evidence is strong and supports the main conclusions.

Reviewer #1 (Public review):

Summary:

In this study, Besson et al. investigate how environmental nutrient signals regulate chromosome biology through the TORC1 signaling pathway in Schizosaccharomyces pombe. Specifically, the authors explore the impact of TORC1 on cohesin function-a protein complex essential for chromosome segregation and transcriptional regulation. Through a combination of genetic screens, biochemical analysis, phospho-proteomics, and transcriptional profiling, they uncover a functional and physical interaction between TORC1 and cohesin. The data suggest that reduced TORC1 activity enhances cohesin binding to chromosomes and improves chromosome segregation, with implications for stress-responsive gene expression, especially in subtelomeric regions.

Strengths:

This work presents a compelling link between nutrient sensing and chromosome regulation. The major strength of the study lies in its comprehensive and multi-disciplinary approach. The authors integrate genetic suppression screens, live-cell imaging, chromatin immunoprecipitation, co-immunoprecipitation, and mass spectrometry to uncover the functional connection between TORC1 signaling and cohesin. The use of phospho-mutant alleles of cohesin subunits and their loader provides mechanistic insight into the regulatory role of phosphorylation. The addition of transcriptomic analysis further strengthens the biological relevance of the findings and places them in a broader physiological context. Altogether, the dataset convincingly supports the authors' main conclusions and opens up new avenues of investigation.

Points that remain open but are appropriately discussed by the authors:

(1) The authors propose that nutrient status influences cohesin regulation. While this is not directly tested under defined nutrient conditions (e.g., by systematically examining cohesin dynamics or phosphorylation across nutrient states), the rationale is well explained in the text, and the study provides a strong foundation for addressing this question in future work.

(2) The upstream signaling cascade downstream of TORC1 remains to be fully elucidated. In particular, the identity of the relevant kinases (e.g., whether Sck1/Sck2 or other effectors are involved) and whether TORC1 directly phosphorylates Mis4 or Psm1 are not resolved. The authors acknowledge these mechanistic gaps, which represent logical next steps rather than shortcomings of the current study.

Reviewer #2 (Public review):

Summary:

In this study the authors follow up on a previous suppressor screen of a temperature-sensitive allele of mis4 (mis4-G1487D), the cohesin loading factor in S. pombe, and identify additional suppressor alleles tied to the S. pombe TORC1 complex. Their analysis suggests that these suppressor mutations attenuate TORC1 activity while enhanced TORC1 activity is deleterious in this context. Suppression of TORC1 activity also ameliorates chromosome segregation and spindle defects observed in the mis4-G1487D strain, although some more subtle effects are not reconstituted. The authors provide evidence that this genetic suppression is also tied to the reconstitution of cohesin loading. Moreover, disrupting TORC1 also enhances Mis4/cohesin association with chromatin (likely reflecting enhanced loading) in WT cells while rapamycin treatment can enhance the robustness of chromosome transmission. These effects likely arise directly through TORC1 or its downstream effector kinases as TORC1 co-purifies with Mis4 and Rad21; these factors are also phosphorylated in a TORC1-dependent fashion. Disrupting Sck2, a kinase downstream of TORC1, also suppresses the mis4-G1487D allele while simultaneous disruption of Sck1 and Sck2 enhances cohesin association with chromatin, albeit with differing effects on phosphorylation of Mis4 and Psm1/Scm1. Phosphomutants of Mis4 and Psm1 that mimic observed phosphorylation states identified by mass spectrometry that are TORC1-dependent also suppressed phenotypes observed in the mis4-G1487D background. Lastly, the authors provide evidence that the mis4-G1487D background and TORC1 mutant backgrounds display an overlap in the dysregulation of genes that respond to environmental conditions.

Overall, the authors provide compelling evidence from genetics, biochemistry and cell biology to support a previously unknown mechanism by which nutrient sensing regulates cohesin loading with implications for the stress response. The technical approaches are generally sound, well-controlled, and comprehensive.

The specific points that I raised in the first review have been addressed by changes/additions to the manuscript or have been determined to be beyond the scope of the study by the authors.

One major question that remains open is the relationship between local changes in cohesin loading and gene expression through this TORC1 regulatory signaling pathway and the details of the underlying mechanisms.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, Besson et al. investigate how environmental nutrient signals regulate chromosome biology through the TORC1 signaling pathway in Schizosaccharomyces pombe. Specifically, the authors explore the impact of TORC1 on cohesin function - a protein complex essential for chromosome segregation and transcriptional regulation. Through a combination of genetic screens, biochemical analysis, phospho-proteomics, and transcriptional profiling, they uncover a functional and physical interaction between TORC1 and cohesin. The data suggest that reduced TORC1 activity enhances cohesin binding to chromosomes and improves chromosome segregation, with implications for stress-responsive gene expression, especially in subtelomeric regions.

Strengths:

This work presents a compelling link between nutrient sensing and chromosome regulation. The major strength of the study lies in its comprehensive and multi-disciplinary approach. The authors integrate genetic suppression screens, live-cell imaging, chromatin immunoprecipitation, co-immunoprecipitation, and mass spectrometry to uncover the functional connection between TORC1 signaling and cohesin. The use of phospho-mutant alleles of cohesin subunits and their loader provides mechanistic insight into the regulatory role of phosphorylation. The addition of transcriptomic analysis further strengthens the biological relevance of the findings and places them in a broader physiological context. Altogether, the dataset convincingly supports the authors' main conclusions and opens up new avenues of investigation.

Weaknesses:

While the study is strong overall, a few limitations are worth noting. The consistency of cohesin phosphorylation changes under different TORC1-inhibiting conditions (e.g., genetic mutants vs. rapamycin treatment) is unclear and could benefit from further clarification. The phosphorylation sites identified on cohesin subunits do not match known AGC kinase consensus motifs, raising the possibility that the modifications are indirect. The study relies heavily on one TORC1 mutant allele (mip1-R401G), and additional alleles could strengthen the generality of the findings. Furthermore, while the results suggest that nutrient availability influences cohesin function, this is not directly tested by comparing growth or cohesin dynamics under defined nutrient conditions.

We thank the reviewer for his overall positive assessment and constructive criticism. We broadly agree with the few limitations he pointed out, which we will comment on below.

(1) The consistency of cohesin phosphorylation changes under different TORC1-inhibiting conditions (e.g., genetic mutants vs. rapamycin treatment) is unclear and could benefit from further clarification.

The basis of our study was to search for suppressor mutants, a situation in which an unviable strain becomes viable. It turns out that the suppressor mutants affect TORC1, necessarily in a partial manner given that TORC1 kinase activity is essential for proliferation. Likewise rapamycin partially inhibits TORC1 and does not prevent proliferation of wild-type S. pombe cells. TORC1 mutants cause a constitutive decrease in activity with possible adaptive effects, whereas rapamycin is applied for a single cell cycle. In addition, it is known that bona fide TORC1 substrates respond differently to rapamycin. Some phosphosites show acute sensitivity, while others are less sensitive or even insensitive (Kang et al., 2013, PMID: 23888043). Therefore, both hypomorphic TORC1 genetic mutants and rapamycin treatment result in partial inhibition of TORC1 kinase activity. While the lists of affected TORC1 substrates may overlap, they are unlikely to be identical. Furthermore, the phosphorylation level of the relevant substrates is not necessarily altered to the same extent. Nevertheless, both conditions suppress the heatsensitive phenotype of the mis4 mutant, although the suppressor effect of rapamycin is weaker. Consequently, some phosphorylation sites involved in mis4-ts suppression may behave similarly in rapamycin and TORC1 mutants (i.e. Psm1-S1022), while others (i.e. Mis4-183) may behave differently.

It is clear that there are phenotypic differences between the suppression of mis4-ts by rapamycin treatment or by genetic alteration of TORC1. This can be seen also in our ChIP analysis of Rad21 distribution at CARs. The trend is upward, but the pattern is not identical. We have added the following text to summarize the above considerations:

“It is important to note at this stage that, although rapamycin and TORC1 mutants both decrease TORC1 kinase activity, the two are not equivalent. The mechanisms by which TORC1 kinase activity is reduced are different, and TORC1 mutants suppress the mis4G1487D phenotype more effectively than rapamycin. It is known that bona fide TORC1 substrates respond differently to rapamycin. Some phosphosites show acute sensitivity, while others are less sensitive or even insensitive (Kang et al, 2013). TORC1 mutants cause a constitutive decrease in activity with possible adaptive effects, whereas rapamycin is applied for a single cell cycle. While the lists of affected TORC1 substrates may overlap, they are unlikely to be identical. Furthermore, the phosphorylation level of the relevant substrates is not necessarily altered to the same extent. It is therefore remarkable that negative regulation of TORC1 by rapamycin or a genetic mutation both alleviate mis4G14878D phenotypes and have a fairly similar effect on cohesin dynamics.”

(2) The phosphorylation sites identified on cohesin subunits do not match known AGC kinase consensus motifs, raising the possibility that the modifications are indirect.

The genetic and biochemical analyses provided in this study show that the AGC kinases Sck1 and Sck2 influence cohesin phosphorylation and function. Whether Sck1, Sck2 or TORC1 directly phosphorylates cohesin components are the next questions to address. The fact that the phosphorylation of Psm1-S1022 and Mis4-S183 were never abolished in the sck1-2 mutants may suggest they are indirectly involved. This should be taken with caution because we have been using deletion mutants. In this situation, cells adapt and other kinases may substitute, at least partially (Plank et al, 2020, PMID: 32102971). Asking whether cohesin components display consensus sites for AGC kinases is a complementary approach. The consensus site for Sck1 and Sck2 is unknown. If we assume some conservation with budding yeast SCH9, the consensus sequence would be RRxS/T. Psm1S1022 (DQMSP) and Mis4-S183 (QLCSP) do not fit the consensus. However, this kind of information should be taken with care as many SCH9-dependent phosphorylation sites did not fall within the consensus in a study using analogue-sensitive AGC kinases and phosphoproteomics (Plank et al, 2020, PMID: 32102971). Alternatively, Sck1-2 may regulate other kinases. Indeed Psm1-S1022 and Mis4-183 lie within CDK consensus sites and Psm1-S1022 phosphorylation is Pef1-dependent. In summary, yes, the changes may be indirect, that remains to be seen, but in any case they are influenced by TORC1 signalling. The following paragraph was added:

“The consensus site for Sck1 and Sck2 is unknown. If we assume some conservation with budding yeast SCH9, the consensus sequence would be RRxS/T. Psm1-S1022 (DQMSP) and Mis4-S183 (QLCSP) do not fit the consensus. However, this should be taken with care as many SCH9-dependent phosphorylation sites did not fall within the consensus in a study using analogue-sensitive AGC kinases and phosphoproteomics (Plank et al, 2020). Alternatively, Sck1-2 may regulate other kinases. Indeed Psm1-S1022 and Mis4-183 lie within CDK consensus sites and Psm1-S1022 phosphorylation is Pef1-dependent.”

(3) The study relies heavily on one TORC1 mutant allele (mip1-R401G), and additional alleles could strengthen the generality of the findings.

It is true that we focused our attention on mip1-R401G, which is present in all the experiments presented. That said, other alleles were used in one or more figures. Five mip1 alleles and one tor2 allele were identified as mis4-ts suppressors (Fig. 1). We have also shown that another mip1 allele, mip1-Y533A, created by another group (Morozumi et al, 2021), is also a suppressor of mis4-ts and affects the phosphorylation of Mis4-S183 and Psm1-S1022 (Fig. 1, Figure 5—figure supplement 1). To this we can add the effect of mutants that render TORC1 hyperactive (Fig. 1E, Fig. 2H) as well as AGC kinase mutants (Figure 5—figure supplement 3.). And finally, the effect of rapamycin. So yes, mip1-R401G has been used extensively, but we have still broadly covered the TORC1 signalling pathway.

(4) Furthermore, while the results suggest that nutrient availability influences cohesin function, this is not directly tested by comparing growth or cohesin dynamics under defined nutrient conditions

We agree that studying the dynamics of cohesin, genome folding and gene expression in relation to nutrient availability is a very exciting topic, and we hope to address these issues in detail in the future.

Reviewer #2 (Public review):

Summary:

In this study, the authors follow up on a previous suppressor screen of a temperaturesensitive allele of mis4 (mis4-G1487D), the cohesin loading factor in S. pombe, and identify additional suppressor alleles tied to the S. pombe TORC1 complex. Their analysis suggests that these suppressor mutations attenuate TORC1 activity, while enhanced TORC1 activity is deleterious in this context. Suppression of TORC1 activity also ameliorates chromosome segregation and spindle defects observed in the mis4-G1487D strain, although some more subtle effects are not reconstituted. The authors provide evidence that this genetic suppression is also tied to the reconstitution of cohesin loading. Moreover, disrupting TORC1 also enhances Mis4/cohesin association with chromatin (likely reflecting enhanced loading) in WT cells, while rapamycin treatment can enhance the robustness of chromosome transmission. These effects likely arise directly through TORC1 or its downstream effector kinases, as TORC1 co-purifies with Mis4 and Rad21; these factors are also phosphorylated in a TORC1-dependent fashion. Disrupting Sck2, a kinase downstream of TORC1, also suppresses the mis4-G1487D allele while simultaneous disruption of Sck1 and Sck2 enhances cohesin association with chromatin, albeit with differing effects on phosphorylation of Mis4 and Psm1/Scm1. Phosphomutants of Mis4 and Psm1 that mimic observed phosphorylation states identified by mass spectrometry that are TORC1-dependent also suppressed phenotypes observed in the mis4-G1487D background. Last, the authors provide evidence that the mis4-G1487D background and TORC1 mutant backgrounds display an overlap in the dysregulation of genes that respond to environmental conditions, particularly in genes tied to meiosis or other "stress".

Overall, the authors provide compelling evidence from genetics, biochemistry, and cell biology to support a previously unknown mechanism by which nutrient sensing regulates cohesin loading with implications for the stress response. The technical approaches are generally sound, well-controlled, and comprehensive.

Specific Points:

(1) While the authors favor the model that the enhanced cohesin loading upon diminished TORC1 activity helps cells to survive harsh environmental conditions, as starvation of S. pombe also drives commitment to meiosis, it seems as plausible that enhanced cohesin loading is related to preparing the chromosomes to mate.

(2) Related to Point 1, the lab of Sophie Martin previously published that phosphorylation of Mis4 characterizes a cluster of phosphotargets during starvation/meiotic induction (PMID: 39705284). This work should be cited, and the authors should interrogate how their observations do or do not relate to these prior observations (are these the same phosphosites?).

We agree this is a possibility and the following paragraph was added in the discussion section:

“TORC1-based regulation of cohesin may be relevant to preparing cells for meiosis. Since nitrogen deprivation stimulates meiosis initiation, subsequent TORC1 down-regulation may regulate the cohesin complex, preparing the chromosomes for fusion and meiosis. A recent phosphoproteomic study conducted by Sophie Martin's laboratory showed that Mis4-S107 phosphorylation increases during cellular fusion (Bérard et al, 2024). It is unknown whether the phosphorylation of S107 is controlled by TORC1 signalling. As the phosphorylation of Mis4-S183 and Psm1-S1022 was not detected in these experiments, the potential involvement of the TORC1-cohesin axis in the sexual programme remains to be investigated.”

(3) It would be useful for the authors to combine their experimental data sets to interrogate whether there is a relationship between the regions where gene expression is altered in the mis4-G1487D strain and changes in the loading of cohesin in their ChIP experiments.

(4) Given that the genes that are affected are predominantly sub-telomeric while most genes are not affected in the mis4-G1487D strain, one possibility that the authors may wish to consider is that the regions that become dysregulated are tied to heterochromatic regions where Swi6/HP1 has been implicated in cohesin loading

We agree that it would be interesting to see if there are correlations between cohesin positioning, heterochromatin and gene expression. That said, this would need to be done at the whole-genome level and include many other parameters (genome folding, histone modifications, Pol2 occupancy). These issues require substantial investment and may be addressed in a follow-up project.

(5) It would be helpful to show individual data points from replicates in the bar graphs - it is not always clear what comprises the data sets, and superplots would be of great help.

We verified that the figure captions clearly indicate the data sets considered, their mean, standard deviation, and statistical analysis method. As for the type of plot, we used the tools at our disposal.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Besson et al. investigate how the nutrient-responsive TORC1 signaling pathway modulates cohesin function in S. pombe. Using a genetic screen, the authors identify TORC1 mutants that suppress the thermosensitive growth defects of a cohesin loader mutant (mis4-G1487D). They show that reducing TORC1 activity-either genetically or pharmacologically-enhances cohesin binding to chromosomal sites (CARs), improves chromosome segregation, and alters the phosphorylation state of cohesin and its loader. They also show, through coimmunoprecipitation, that TORC1 and cohesin physically associate, and that this functional interaction extends to the transcriptional regulation of stress-responsive, subtelomeric genes. Together, the data suggest that environmental cues influence chromosome stability and gene expression via a TORC1-cohesin axis.

Overall, the study is well-supported by thoughtful genetic epistasis analyses and a combination of genetic, biochemical, cell biological, and transcriptomic approaches. While not all data are equally strong, the cumulative evidence convincingly supports the authors' conclusions.

Specific Concerns and Suggestions

(1) Figure 2A - Division rates of wild-type and mip1-R401G cells are missing and should be provided for proper comparison.

This is now done in revised Figure 2A. We also made a change in the manuscript, replacing “The mip1-R401G mutation efficiently suppressed the proliferation and viability defects (Figure 2A)” by “The mip1-R401G mutation efficiently attenuated the proliferation and viability defects (Figure 2A)”, to acknowledge the fact that the proliferation rate did not return to wild-type levels.

(2) Figure 3 - Figure Supplement 1 - The authors claim that "Rapamycin treatment during a single cell cycle provoked a similar effect although less pronounced." However, for most CARs, the effect appears insignificant. This should be acknowledged in the text.

The text has been changed accordingly:

“Rapamycin treatment during a single cell cycle provoked a similar stimulation of Rad21 binding at CARs (Figure 3—figure supplement 1), albeit with noticeable differences. In mis4+ cells, both mip1-R401G and rapamycin induced a significant increase in Rad21 binding at several CARs (tRNA-left, cc2, 3323, NTS, Tel1-R). However, some CARs that exhibited increased Rad21 binding in the mip1 mutant did not respond significantly to rapamycin (dg2-R, tRNA-R). Conversely, rapamycin (but not mip1-R401G) induced a significant increase in Rad21 binding at imr2-L and CAR1806 (Figure 3D and Figure 3— figure supplement 1). In the mis4-G1487D mutant background, mip1-R401G induced a significant increase in Rad21 binding at all examined sites (Figure 3B). Similarly, rapamycin did increase Rad21 binding at all sites but only at the Tel1-R site did this reach statistical significance (Figure 3—figure supplement 1).”

(3) Figure 4 - The analysis of interactions between TORC1 and the cohesin complex is somewhat limited. The authors may wish to test interactions between Mip1 and cohesin subunits (e.g., Rad21). More interestingly, it would be valuable to explore whether MIP1 mutations that suppress cohesin mutants affect the interaction between Tor2 and Rad21.

We have added some additional data that answer this question (Figure 4—figure supplement 1) and a paragraph in the manuscript:

“Tor2, the kinase subunit of TORC1, is particularly well detected in Rad21 and Mis4 coimmunoprecipitation experiments (Figure 4 and Figure 4—figure supplement 1). To determine whether the R401G mutation in Mip1 affects these interactions, coimmunoprecipitation experiments were repeated in both the mip1-R401G and mip1+ contexts. The data obtained indicate that Tor2 co-immunoprecipitation with Mis4 and Rad21 is largely unaffected by the mip1-R401G mutation (Figure 4—figure supplement 1). If mip1-R401G affects the regulation of cohesin by TORC1, this does not appear to stem from a gross defect in their interaction, at least at this level of resolution.”

(4) Figure 5 - There appears to be a lack of correlation between cohesin subunit phosphorylation in TORC1-reducing mutants and in response to rapamycin. The reason for this discrepancy is unclear.

This point was addressed in the previous section (Public review, reviewer 1, point 1). The response is pasted below:

The basis of our study was to search for suppressor mutants, a situation in which an unviable strain becomes viable. It turns out that the suppressor mutants affect TORC1, necessarily in a partial manner given that TORC1 kinase activity is essential for proliferation. Likewise rapamycin partially inhibits TORC1 and does not prevent proliferation of wild-type S. pombe cells. TORC1 mutants cause a constitutive decrease in activity with possible adaptive effects, whereas rapamycin is applied for a single cell cycle. In addition, it is known that bona fide TORC1 substrates respond differently to rapamycin. Some phosphosites show acute sensitivity, while others are less sensitive or even insensitive (Kang et al., 2013, PMID: 23888043). Therefore, both hypomorphic TORC1 genetic mutants and rapamycin treatment result in partial inhibition of TORC1 kinase activity. While the lists of affected TORC1 substrates may overlap, they are unlikely to be identical. Furthermore, the phosphorylation level of the relevant substrates is not necessarily altered to the same extent. Nevertheless, both conditions suppress the heatsensitive phenotype of the mis4 mutant, although the suppressor effect of rapamycin is weaker. Consequently, some phosphorylation sites involved in mis4-ts suppression may behave similarly in rapamycin and TORC1 mutants (i.e. Psm1-S1022), while others (i.e. Mis4-183) may behave differently.

It is clear that there are phenotypic differences between the suppression of mis4-ts by rapamycin treatment or by genetic alteration of TORC1. This can be seen also in our ChIP analysis of Rad21 distribution at CARs. The trend is upward, but the pattern is not identical. We have added the following text to summarize the above considerations:

“It is important to note at this stage that, although rapamycin and TORC1 mutants both decrease TORC1 kinase activity, the two are not equivalent. The mechanisms by which TORC1 kinase activity is reduced are different, and TORC1 mutants suppress the mis4G1487D phenotype more effectively than rapamycin. It is known that bona fide TORC1 substrates respond differently to rapamycin. Some phosphosites show acute sensitivity, while others are less sensitive or even insensitive (Kang et al, 2013). TORC1 mutants cause a constitutive decrease in activity with possible adaptive effects, whereas rapamycin is applied for a single cell cycle. While the lists of affected TORC1 substrates may overlap, they are unlikely to be identical. Furthermore, the phosphorylation level of the relevant substrates is not necessarily altered to the same extent. It is therefore remarkable that negative regulation of TORC1 by rapamycin or a genetic mutation both alleviate mis4G14878D phenotypes and have a fairly similar effect on cohesin dynamics.”

(5) The phosphorylation sites examined on cohesin subunits are not canonical AGC kinase consensus motifs, suggesting they are unlikely to be direct targets of Sck1 or Sck2. I suggest that this point should be mentioned in the manuscript.

This is now done:

“The consensus site for Sck1 and Sck2 is unknown. If we assume some conservation with budding yeast SCH9, the consensus sequence would be RRxS/T. Psm1-S1022 (DQMSP) and Mis4-S183 (QLCSP) do not fit the consensus. However, this should be taken with care as many SCH9-dependent phosphorylation sites did not fall within the consensus in a study using analogue-sensitive AGC kinases and phosphoproteomics (Plank et al, 2020). Alternatively, Sck1-2 may regulate other kinases. Indeed Psm1-S1022 and Mis4-183 lie within CDK consensus sites and Psm1-S1022 phosphorylation is Pef1-dependent.”

(6) Figure 5 - Figure Supplement 3 - The reduction in Psm1 phosphorylation in the sck1Δ sck2Δ double mutant is not convincing without replicates and statistical analysis.

This is now done and the data are presented in Figure 5—figure supplement 3. Panel D shows the data for Psm1-S1022p and Panel E for Mis4-S183p. Each graph shows the mean ratios +/- SD from 3 experiments.

(7) Figure 5C - It would be helpful if the authors validated the effect of pef1 deletion on Mis4 phosphorylation by Western blotting, rather than relying solely on mass spectrometry data.

This is now done. The data appears in Figure 5—figure supplement 2, panel B.

(8) The statement: "The frequency of chromosome segregation defects of mis4‐G1487D was markedly reduced in a sck2‐deleted background and further decreased by the additional deletion of sck1 (Figure 5-figure supplement 3)" is not supported by the data. According to the figure, the difference between sck2Δ and sck1Δ sck2Δ is not statistically significant.

The sentence was changed to:

“The frequency of chromosome segregation defects in the mis4-G1487D strain remained unchanged in a sck1-deleted background, but was significantly reduced when either the sck2 or both the sck1 and sck2 genes were deleted (Figure 5—figure supplement 3).”

(9) Figure 6A - The data shown are not convincing. The double mutants carrying the phosphomimetic and phospho-null psm1 alleles should be shown on the same plate for direct comparison.

This is now done. The new data are shown Figure 6A.

(10) Figure 6E - The wild-type control is missing. Including it would provide an essential reference point to assess whether the mutants rescue cohesin binding to wild-type levels.

This is true that the effects were small when compared to wild-type but still significant when compared to mis4-G1487D. The comparison with wild-type is now available in Figure 6—figure supplement 1 and the paragraph was modified accordingly:

“Cohesin binding to CARs as assayed by ChIP tend to increase for the mutants mimicking the non-phosphorylated state and to decrease with the phospho-mimicking forms (Figure 6E). The rescue of mis4-G1487D by the non-phosphorylatable form was modest but significant, notably within centromeric regions (imr2-L, dg2-R) and at the telomere (Tel1-R) site (Figure 6E and see Figure 6—figure supplement 1 for comparison with wild-type levels). Conversely, the mutant mimicking the phosphorylated state displayed a significant reduction of Rad21 binding at those sites as well as to several other sites at the centromere (cc2, tRNA-R), CAR2898, and at the ribosomal non-transcribed spacer site NTS).”

Limitations of the Study (not requiring additional experiments for publication, but worth noting).

(11) The authors suggest that nutrient status affects cohesin, but this is not directly demonstrated-e.g., by comparing growth or cohesin dynamics or phosphorylation under defined nutrient conditions. That said, the paper is sufficiently detailed to allow this question to be addressed in follow-up work.

We agree that studying the dynamics of cohesin, genome folding and gene expression in relation to nutrient availability is a very exciting topic, and we hope to address these issues in detail in the future.

(12) The upstream signaling cascade remains unresolved. The identity of kinases downstream of TORC1 (e.g., whether Sck1/Sck2 or other factors are responsible) and whether TORC1 directly phosphorylates Mis4 or Psm1 are not established.

This is something we can all agree on, and it might be something we look at in a future project.

(13) The conclusions rely heavily on one TORC1 mutant allele (mip1-R401G). While this allele is informative, additional alleles or orthogonal methods could further support the generality of the findings.

It is true that we focused our attention on mip1-R401G, which is present in all the experiments presented. That said, other alleles were used in one or more figures. Five mip1 alleles and one tor2 allele were identified as mis4-ts suppressors (Fig. 1). We have also shown that another mip1 allele, mip1-Y533A, created by another group (Morozumi et al, 2021), is also a suppressor of mis4-ts and affects the phosphorylation of Mis4-S183 and Psm1-S1022 (Fig. 1, Figure 5—figure supplement 1). To this we can add the effect of mutants that render TORC1 hyperactive (Fig. 1E, Fig. 2H) as well as AGC kinase mutants (Figure 5—figure supplement 3.) and finally, the effect of a transient treatment with rapamycin. So yes, mip1-R401G has been used extensively, but we have still broadly covered the TORC1 signalling pathway.

Reviewer #2 (Recommendations for the authors):

(1) Given the lack of CTCF in fission yeast, it is worth noting that cohesin ChIP data nonetheless can predict topological domains, which reinforces its important role in dictating chromatin folding (PMID: 39543681).

We thank the reviewer for this suggestion. We now refer to this study in the discussion section.

(2) Providing context for the S. pombe nomenclature for the conserved cohesin subunits would help the reader navigate the manuscript, possibly using a cartoon as for the TORC complexes. For example, Psm1 (aka Smc1) is not introduced and therefore its phosphorylation comes into the manuscript without explanation.

Cohesin subunits and their names are given in the introduction section.

eLife Assessment

This convincing study examines a novel interaction of RAB5 with VPS34 complex II. Structural data are combined with site-directed mutagenesis, sequence analysis, biochemistry, yeast mutant analysis, and prior data on RAB1-VPS34 and RAB5-VPS34 interactions to provide a new perspective on how RAB GTPases recruit related but distinct VPS34 complexes to different organelles. The judgment is that this work represents a fundamental advance in our understanding of VPS34 localization and regulation.

Reviewer #1 (Public review):

Summary:

This manuscript presents high resolution cryoEM structures of VPS34-complex II bound to Rab5A at 3.2A resolution. The Williams group previously reported the structure of VPS34 complex II bound to Rab5A on liposomes using tomography, and therefore the previous structure, although very informative, was at lower resolution.

The first new structure they present is of the 'REIE>AAAA' mutant complex bound to RAB5A. The structure resembles the previously determined one except an additional molecule of RAB5A was observed bound to the complex in a new position, interacting with the solenoid of VPS15.

Although this second binding site exhibited reduced occupancy of RAB5A in the structure, the authors determined an additional structure in which the primary binding site was mutated to prevent RAB5A binding ('REIE>ERIR'). In this structure, there is no RAB5A bound to the primary binding site on VPS34, but the RAB5A bound to VPS15 now has strong density. The authors note that the way in which RAB5A interacts with each site is distinct, though both interfaces involve the switch regions. The authors confirm the location of this additional binding site using HDX-MS.

The authors then determine multiple structures of the wild-type complex bound to RAB5A from a single sample, as they use 3D classifications to separate out versions of the complex bound to 0, 1, or 2 copies of RAB5A. Overall the structure of VPS34-Complex II does not change between the different states, and the data indicate that both RAB5A binding sites can be occupied at the same time.

The authors then design a new mutant form of the complex (SHMIT>DDMIE) that is expected to disrupt the interaction at the secondary site between VPS15 and RAB5A. This mutation had a minor impact on the Kd for RAB5A binding, but when combined with the REIE>ERIR mutation of the primary binding site, RAB5A binding to the complex was abolished.

Comparison of sequences across species indicated that the RAB5A binding site on VPS15 was conserved in yeast while the RAB5A binding site on VPS34 is not.

The authors tested the impact of a correspond yeast Vps15 mutation (SHLITY>DDLIEY) predicted to disrupt interaction with yeast Rab5/Vps21, and found this mutant Vps15 protein was mislocalized and caused defective CPY processing.

The authors then compare these structures of the RAB5A-class II complex to recently published structures from the Hurley group of the RAB1A-class I complex, and find that in both complexes the Rab protein is bound to the VPS34 binding site in a somewhat similar manner. However, a key difference is the position of VPS34 is slightly different in the two complexes because of the unique ATL14L and UVRAG subunits in the class I and class II complexes, respectively. This difference creates a different RAB binding pocket that explains the difference in RAB specificity between the two complexes.

Finally, the higher resolution structures enable the authors to now model portions of BECLIN1 and UVRAG that were not previously modeled in the cryoET structure.

Strengths:

Overall I found this to be an interesting and comprehensive study of the structural basis for interaction of RAB5A with VPS34-complex II. The authors have performed experiments to validate their structural interpretations, and they present a clear and thorough comparative analysis of the Rab binding sites in the two different VPS34 complexes. The result is a much better understanding of how two different Rab GTPases specifically recruit two different, but highly similar complexes to the membrane surface.

Weaknesses:

No significant weaknesses noted.

Reviewer #2 (Public review):

The work by Spokaite et al describes the discovery of a novel Rab5 binding site present in complex II of class III PI3K using a combination of HDX and Cryo EM. Extensive mutational and sequence analysis define this as the primordial Rab5 interface. The data presented are convincing that this is indeed a biologically relevant interface, and is important in defining mechanistically how vps34 complexes are regulated.

This paper is a very nice expansion of their previous cryo-ET work from 2021, and is an excellent companion piece on high resolution cryo-EM of the complex I class III complex bound to Rab1 from the Hurley lab in 2025. Overall, this work is of excellent technical quality, and answers important unexplained observations on some unexpected mutational analysis from the previous work.

They used their increased affinity vps34 mutant to determine the 3.2 ang structure of Rab5 bound to vps34-CII. Clear density was seen for the original Rab5 interface, but an additional site was observed. Based on this structure they mutated out the vps34 interface, allowing for a high resolution structure of the Rab5 bound at the Vps15 interface.

They extensively validated the vps15 interface in the yeast variant of vps34, showing that the Vp215-Rab5 (Vps21) interface identified is critical in controlling complex II vps34 recruitment.

The major strengths of this paper are that the experiments appear to be done carefully and rigorously and I have very few experimental suggestions.

Here is what I recommend based on some very minor weaknesses I observed

(1) My main concern has to do a little bit with presentation. My main issue is how the authors use mutant description. They clearly indicate the mutant sequence in the human isoform (for example see Fig 2A, Vps15 described as 579-SHMIT-583>DDMIE), however, when they shift to the yeast version they shift to saying vps15 mutant, but don't define the mutant, Fig 2G). I would recommend they just include the same sequence numbering and WT to mutant replacement every time a new mutant (or species) is described. It is always easier to interpret what is being shown when the authors are jumping between species when the exact mutant is included. This is particularly important in this paper, where we are jumping between both different subunits and different species, so clear description in figure/figure legends makes it much easier to read for non-specialists.

(2) The HDX data very clearly shows that Rab5 is likely able to bind at both sites, which back ups the cryo EM data nicely. I am slightly confused by some of the HDX statements described in the methods.

(3) The authors state "Only statistically significant peptides showing a difference greater than 0.25 Da and greater than 5% for at least two timepoints were kept." This seems to be confusing why they required multiple timepoints, and before they also describe that they required a p value of less than 0.05. It might be clearer to state that significant differences required a 0.25 Da, 5%, and p value of <0.05 (n=3). Also what do they mean by kept? Does this mean that they only fully processed the peptides with differences.

(4) They show peptide traces for a selection in the supplement, but it would be ideal to include the full set of HDX data as an excel file, including peptides with no differences as there is a lot of additional information (deuteration levels for everything) that would be useful to share, as recommended from the Masson et al 2019 recommendations paper. This may be attached but this reviewer could not see an example of it in the shared data dropbox folder.

Comments on revisions:

The authors have addressed all of my issues.

Reviewer #3 (Public review):

Summary:

The manuscript of Spokaite et al. focuses on the Vps34 complex involved in PI3P production. This complex exists in two variants, one (class I) specific for autophagy, and a second one (class II) specific for the endocytic system. Both differ only in one subunit. The authors previously showed that the Vps34 complexes interact with Rab GTPases, Rab1 or Rab5 (for class II), and the identified site was found at Vps34. Now, the authors identify a conserved and overlooked Rab5 binding site in Vps15, which is required for the function of the Class II complex. In support of this, they show cryo-EM data with a second Rab5 bound to Vps15, identify the corresponding residues, and show by mutant analysis that impaired Rab5 binding also results in defects using yeast as a model system.

Overall, this is a most complete study with little to criticize. The paper shows convincingly that the two Rab5 binding sites are required for Vps34 complex II function, with the Vps15 binding site being critical for endosomal localization. The structural data is very much complete. What I am missing are a few controls that show that the mutations in Vps15 do not affect autophagy. I also found the last paragraph of the results section a bit out of place, even though this is a nice observation that the N-terminal part of BECLIN has these domains. However, what does it add to the story?

Comments on revisions:

The authors answered all my questions. I have no further requests.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript presents high-resolution cryoEM structures of VPS34-complex II bound to Rab5A at 3.2A resolution. The Williams group previously reported the structure of VPS34 complex II bound to Rab5A on liposomes using tomography, and therefore, the previous structure, although very informative, was at lower resolution.

The first new structure they present is of the 'REIE>AAAA' mutant complex bound to RAB5A. The structure resembles the previously determined one, except that an additional molecule of RAB5A was observed bound to the complex in a new position, interacting with the solenoid of VPS15.

Although this second binding site exhibited reduced occupancy of RAB5A in the structure, the authors determined an additional structure in which the primary binding site was mutated to prevent RAB5A binding ('REIE>ERIR'). In this structure, there is no RAB5A bound to the primary binding site on VPS34, but the RAB5A bound to VPS15 now has strong density. The authors note that the way in which RAB5A interacts with each site is distinct, though both interfaces involve the switch regions. The authors confirm the location of this additional binding site using HDX-MS.

The authors then determine multiple structures of the wild-type complex bound to RAB5A from a single sample, as they use 3D classifications to separate out versions of the complex bound to 0, 1, or 2 copies of RAB5A. Overall, the structure of VPS34-Complex II does not change between the different states, and the data indicate that both RAB5A binding sites can be occupied at the same time.

The authors then design a new mutant form of the complex (SHMIT>DDMIE) that is expected to disrupt the interaction at the secondary site between VPS15 and RAB5A. This mutation had a minor impact on the Kd for RAB5A binding, but when combined with the REIE>ERIR mutation of the primary binding site, RAB5A binding to the complex was abolished.

Comparison of sequences across species indicated that the RAB5A binding site on VPS15 was conserved in yeast,while the RAB5A binding site on VPS34 is not.

The authors tested the impact of a corresponding yeast Vps15 mutation (SHLITY>DDLIEY) predicted to disrupt interaction with yeast Rab5/Vps21, and found that this mutant Vps15 protein was mislocalized and caused defective CPY processing.

The authors then compare these structures of the RAB5A-class II complex to recently published structures from the Hurley group of the RAB1A-class I complex, and find that in both complexes the Rab protein is bound to the VPS34 binding site in a somewhat similar manner. However, a key difference is that the position of VPS34 is slightly different in the two complexes because of the unique ATL14L and UVRAG subunits in the class I and class II complexes, respectively. This difference creates a different RAB binding pocket that explains the difference in RAB specificity between the two complexes.

Finally, the higher resolution structures enable the authors to now model portions of BECLIN1 and UVRAG that were not previously modeled in the cryoET structure.

Strengths:

Overall, I found this to be an interesting and comprehensive study of the structural basis for the interaction of RAB5A with VPS34-complex II. The authors have performed experiments to validate their structural interpretations, and they present a clear and thorough comparative analysis of the Rab binding sites in the two different VPS34 complexes. The result is a much better understanding of how two different Rab GTPases specifically recruit two different, but highly similar complexes to the membrane surface.

Weaknesses:

No significant weaknesses were noted.

Reviewer #2 (Public review):

Summary:

The work by Spokaite et al describes the discovery of a novel Rab5 binding site present in complex II of class III PI3K using a combination of HDX and Cryo EM. Extensive mutational and sequence analysis define this as the primordial Rab5 interface. The data presented are convincing that this is indeed a biologically relevant interface, and is important in defining mechanistically how VPS34 complexes are regulated.

This paper is a very nice expansion of their previous cryo-ET work from 2021, and is an excellent companion piece on high-resolution cryo-EM of the complex I class III complex bound to Rab1 from the Hurley lab in 2025. Overall, this work is of excellent technical quality and answers important unexplained observations on some unexpected mutational analysis from the previous work.

They used their increased affinity VPS34 mutant to determine the 3.2 ang structure of Rab5 bound to VPS34-CII. Clear density was seen for the original Rab5 interface, but an additional site was observed. Based on this structure, they mutated out the VPS34 interface, allowing for a high-resolution structure of the Rab5 bound at the VPS15 interface.

They extensively validated the VPS15 interface in the yeast variant of VPS34, showing that the Vp215-Rab5 (VPS21) interface identified is critical in controlling complex II VPS34 recruitment.

The major strengths of this paper are that the experiments appear to be done carefully and rigorously, and I have very few experimental suggestions.

Here is what I recommend based on some very minor weaknesses I observed

(1) My main concern has to do a little bit with presentation. My main issue is how the authors use mutant description. They clearly indicate the mutant sequence in the human isoform (for example, see Figure 2A, VPS15 described as 579-SHMIT-583>DDMIE); however, when they shift to the yeast version, they shift to saying VPS15 mutant, but don't define the mutant, Figure 2G). I would recommend they just include the same sequence numbering and WT to mutant replacement every time a new mutant (or species) is described. It is always easier to interpret what is being shown when the authors are jumping between species, when the exact mutant is included. This is particularly important in this paper, where we are jumping between different subunits and different species, so a clear description in the figure/figure legends makes it much easier to read for non-specialists.

The reviewer has made an excellent point here. To clarify the yeast mutation, we have revised the manuscript main text to refer to the yeast mutant as SHLITY>DDLIEY, and we have added this to the legend for Figs. 2F,G.

(2) The HDX data very clearly shows that Rab5 is likely able to bind at both sites, which back ups the cryo EM data nicely. I am slightly confused by some of the HDX statements described in the methods.

(3) The authors state, "Only statistically significant peptides showing a difference greater than 0.25 Da and greater than 5% for at least two timepoints were kept." This seems to be confusing as to why they required multiple timepoints, and before they also describe that they required a p-value of less than 0.05. It might be clearer to state that significant differences required a 0.25 Da, 5%, and p-value of <0.05 (n=3). Also, what do they mean by kept? Does this mean that they only fully processed the peptides with differences?

(4) They show peptide traces for a selection in the supplement, but it would be ideal to include the full set of HDX data as an Excel file, including peptides with no differences, as there is a lot of additional information (deuteration levels for everything) that would be useful to share, as recommended from the Masson et al 2019 recommendations paper. This may be attached, but this reviewer could not see an example of it in the shared data dropbox folder.

We have revised the HDX method description to clarify. All peptides were kept and fully processed. However, for the results displayed, we have illustrated only peptides meeting the criteria described.

The Excel file for all peptides (as recommended by Masson et al) was deposited with PRIDE, with the identifier with the dataset identifier PXD061277, in addition, we have included this excel file in our supplementary material.

Reviewer #3 (Public review):

Summary:

The manuscript of Spokaite et al. focuses on the Vps34 complex involved in PI3P production. This complex exists in two variants, one (class I) specific for autophagy, and a second one (class II) specific for the endocytic system. Both differ only in one subunit. The authors previously showed that the Vps34 complexes interact with Rab GTPases, Rab1 or Rab5 (for class II), and the identified site was found at Vps34. Now, the authors identify a conserved and overlooked Rab5 binding site in Vps15, which is required for the function of the Class II complex. In support of this, they show cryo-EM data with a second Rab5 bound to Vps15, identify the corresponding residues, and show by mutant analysis that impaired Rab5 binding also results in defects using yeast as a model system.

Overall, this is a most complete study with little to criticize. The paper shows convincingly that the two Rab5 binding sites are required for Vps34 complex II function, with the Vps15 binding site being critical for endosomal localization. The structural data is very much complete.

Weaknesses:

What I am missing are a few controls that show that the mutations in Vps15 do not affect autophagy. I am wondering if this mutant is still functional in autophagy. This can be simply tested by sorting of Atg8 to the vacuole lumen using established assays or by following PhoΔ60 sorting. This analysis would reveal that the corresponding mutant is specific for the Class II complex.

One of the first noted features of the VPS34 complexes was that the ATG14-containing complex (VPS34-CI) is important for autophagy, while the VPS38 (yeast orthologue of UVRAG) subunit characteristic of VPS34-CII is important for endocytic sorting (PMID 11157979). However, the VPS34, VPS15 and BECLIN1 subunits are required are present in both complexes, as such, mutations of them may affect both processes.

We agree with the reviewer that is an important undertaking to examine the effect of the SHLITY>DDLIEY mutation in yeast Vps15 on autophagy. However, the focus of the current manuscript is VPS34-complex II and RAB5 interaction/activation. An autophagy effect would be more relevant for VPS34 complex I and RAB1. We have not presented any results for human VPS34-complex I - RAB1 nor yeast Vps34-complex I – Ypt1 (yeast RAB1 orthologue). We are preparing another manuscript focusing entirely on this, and it is not a simple story. While we think this is an important question, we believe that this is beyond the scope of the current manuscript.

It would be helpful if the authors could clarify whether they believe that Vps34 kinase activity is stimulated by Rab binding or whether this stimulation is a consequence of better membrane localization of Vps34. In other words, is the complex active with soluble PI3P in solution, and does the activity change if Rab5 is added to the complex? This might have been addressed in the past, but I did not see evidence for this, as the authors only addressed the activity of the Vps34 complexes on membranes.

The reviewer has raised an excellent question, which was addressed briefly in the introduction to the manuscript. We have now somewhat expanded on these issues near the end of the discussion in the revised manuscript. In our previously published study, we found that soluble RAB5-GTP did not stimulate the complex II activity (supplementary figure 2b of PMID: 33692360). This is consistent with our finding in this manuscript showing that RAB5 did not cause large conformational changes in solution. However, our previous single-molecule study showed that once complex II is recruited to the membrane by RAB5, and RAB5 increases the turnover rate on membranes, indicating an additional allosteric activation (Figure 7 of PMID: 33137306). This study indicated that the primary the role of RAB5 is to anchor complex II on the membrane. Once the complex is anchored on the membrane by RAB5, the kinase domain is in the vicinity of its substrate, PI, leading to higher turnover.

The Echelon Class III PI3K ELISA Kit (Echelon, K-3000) comes with a soluble PI, diC8 to measure the VPS34 activity, and it is certainly active with this soluble substrate. However, if the substrate is in membranes, the VPS34 activity is greatly dependent on the character of the membrane.

I also found the last paragraph of the results section a bit out of place, even though this is a nice observation that the N-terminal part of BECLIN has these domains. However, what does it add to the story?

The reviewer is correct that the high-resolution features of BECLIN1 at the base of the V-shaped complex that we observed are not related to RAB5 binding, but they are characteristic of VPS34-CII and likely to be important for the specific role of VPS34-CII. This is the first high-resolution structure of the VPS34-CII that has been reported, and we believe it would be irresponsible not to briefly describe them, since they are unique to VPS34-CII. For this reason, we have placed this section at the end of the results, and we now clarify that we do not see a relevance to RAB5 function, but we describe the arrangement of a region (the BH3) that has been functionally noted in many previous studies, in the absence of a structure.

Reviewing Editor Comments:

Please address the following suggestions for minor changes to the manuscript. Use your best scientific judgment in addressing the comments and describe the modifications together with your reasoning in a cover letter. We look forward to seeing the revised version of this very nice study.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I found a portion of the description of the cryoEM complexes on the top of page 9 to be redundant with similar descriptions near the top of page 7, and it was not clear to me at first that these were describing the same structures. Part of my confusion was due to the redundancy, including the statement near the bottom of page 7: 'Models were built and refined for all RAB5associated VPS34-CII assemblies', and then the similar statement on page 9: 'We fit and refined atomic models into both densities'. I believe these are describing the same models? To clarify for the reader, perhaps on page 9, the authors could begin this part with a statement such as "as described above", and eliminate the redundant descriptions.

The reviewer is correct. Both sections describe the same set of cryo-EM classes from the same sample. The only difference is what we analysed in the two sections: number of RAB5s bound in the first section and the effect of RAB5 binding in the second section. We have revised the text to make this clear, and to make the second section more succinct.

Reviewer #3 (Recommendations for the authors):

(1) The authors show nicely that a mutation in Vps15 disrupts binding to Vps21 in vivo, with defects in the endocytic pathway as analyzed by CPY sorting. I am wondering if this mutant is still functional in autophagy. This can be simply tested by sorting of Atg8 to the vacuole lumen using established assays or by following Pho∆60 sorting. This analysis would reveal that the corresponding mutant is specific for the Class II complex. If the authors were to find evidence that this Vps15 mutant also affects autophagy, it would indicate that there is possibly also another Rab1 binding site in Vps15.

As we stated above, an autophagy effect would be more relevant for VPS34 complex I and RAB1. We have not presented any results for human VPS34-complex I - RAB1 nor yeast Vps34-complex I – Ypt1 (yeast RAB1 orthologue). We are preparing another manuscript focusing entirely on this, and it is not a simple story. While we think this is an important question, we believe that this is beyond the scope of the current manuscript.

(2) It would be helpful if the authors could clarify whether they believe that Vps34 kinase activity is stimulated by Rab binding or whether this stimulation is a consequence of better membrane localization of Vps34. In other words, is the complex active with soluble PI3P in solution, and does the activity change if Rab5 is added to the complex? This might have been addressed in the past, but I did not see evidence for this, as the authors only addressed the activity of the Vps34 complexes on membranes.

As in our response to reviewer #3 above, this point was addressed in previous publications and was described in the introduction to our manuscript.

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:

The 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 that the parasites were exposed to. 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) that they demonstrate is not detrimental to parasite viability or replication. This enabled them to avoid potential complications of 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.

Impact and conclusions:

The study shows that protein export, including PfEMP1 and PSAC, are accelerated in response to mild heat shock. This has implications for disease severity as well as our understanding of protein trafficking in these unique organisms. There is increasing interest in asymptomatic infections, which have been proposed to be a major reservoir for transmission and generally are not associated with fever. It will be interesting to consider whether reduced (or slower) trafficking of these proteins has a selective advantage for parasites in asymptomatic infections.

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?

Comments on Revision:

Although in any study there are going to be residual weaknesses, this reviewer is happy to see that the authors have gone to lengths to address many of my main concerns, and also those of other reviewers.

Reviewer #3 (Public review):

Summary:

In this paper it is established that high fever-like 39oC temperatures cause parasite infected red blood cells become stickier. It is thought that high temperatures might help the spleen to destroy parasite infected cells, so they become stickier to remain trapping 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 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:

Minor weaknesses in the original version have now been satisfactorily addressed with additional work which is very convincing.

Author Response:

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

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.

We thank all reviewers for their constructive feedback on our manuscript.

We believe we have addressed all the questions in the rebuttal below in writing, including planned experiments we will perform to strengthen the conclusions of the manuscript.

Public Reviews:

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.

New Results:

We performed sorbitol sensitivity assays on >20 hours post-infection iRBCs following heat stress in the presence and absence of the PSAC inhibitor furosemide. These additional experiments were added to the supplementary figures (Supplementary Figure 3). Importantly, sorbitol-mediated lysis of iRBCs, with or without prior heat stress, was reduced when furosemide was present, demonstrating that the observed effect is likely PSAC-dependent. We also observed that uninfected RBCs did not lyse with sorbitol, regardless of heat stress, confirming that the effect is specific to infected cells.

(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.

New Results:

Immunofluorescence microscopy, including the localisation of the two HA-tagged proteins (PF3D7_1039000 and PF3D7_0702500), has been repeated and higher-quality images are now included in the updated manuscript (Supplementary Figures 9 and 11). These images include co-staining with the P. falciparum proteins KAHRP and SPB1 to assess possible co-localisations. Furthermore, following the reviewer’s suggestion, we have softened the statement regarding PF3D7_1039000-HA to better reflect the data, changing “...does not colocalise” to “...does not strongly colocalise”.

(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 possibly including 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 in the 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, here we focused on enhanced protein export using multiple complementary approaches, and have chosen to address rigidity questions in a different study.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

As mentioned above, a second time point in many of the assays (for example, 36 hrs or later) would be useful to determine if heat stress simply accelerates trafficking of proteins to the RBC or if instead it results in an overall increase in trafficking.

As mentioned earlier: 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. This is true for the DMSO (control wildtype resembling) HA-tagged lines of HSP70x and PF3D7_072500 (Supplementary Figures 9 and 12 respectively). The end level of VAR2CSA is the same in both conditions, but at 24 hours post infection it is higher following heat stress, indicating that trafficking is accelerated.

In the text, the authors frequently mention changes in the parasites' phenotype in response to heat stress; however, the way it is described is a bit ambiguous and can be confusing. For example, on page 3, they state that "Following heat stress, significantly more iRBCs (57.6% +/-19.4%) cytoadhered.....". From this sentence, it is not initially clear if the end result is cytoadherence of 57.6% of iRBCs or if this refers to an increase of 57.6%. This could be stated explicitly (e.g., "an increase of 57.6% +/- 19.4%") to avoid confusion. Similar descriptions of the results are found throughout the paper.

We agree this is confusing and altered the text accordingly.

The authors might consider citing and discussing the paper from Andrade et al (Nat Med, 2020, 26:1929-1940), which describes longer circulation times (less cytoadherence) by parasites in the dry season (asymptomatic patients) than in febrile patients in the wet season (stronger cytoadhesion of younger stages). This would seem to be consistent with the data presented here.

We are aware of the Andrade study, but chose not to cite it in this context since the reported differences in cytoadhesion appear more consistent with PfEMP1 expression levels, as hypothesized by the authors, than with altered trafficking.

Reviewer #2 (Recommendations for the authors):

General comments on the text:

(1) "Approximately 10% of the proteins encoded by P. falciparum are predicted to be exported beyond the parasite plasma membrane (PPM) into the parasitophorous vacuole lumen (PVL) and subsequently across the parasitophorous vacuole membrane (PVM) into the RBC cytosol."

To my knowledge, it has not been really demonstrated that all exported proteins take this route (transfer step in the PVL), and how transmembrane proteins transfer from the parasite to the erythrocyte is still poorly understood. I recommend that the authors rephrase this for precision.

We agree with this reviewer and will change the statement.

Changes:

We have clarified these statements to accurately reflect the current understanding of protein export. Approximately 10% of P. falciparum encoded proteins are predicted to be exported beyond the parasite plasma membrane, with many thought to pass through the parasitophorous vacuole lumen (PVL) and parasitophorous vacuole membrane (PVM) into the RBC cytosol, although the exact routes for transmembrane proteins are not fully understood.”

(2) "Charnaud et al. 25, but not Cobb et al. 26, found HSP70x to be essential for normal PfEMP1 trafficking, although both studies concluded that HSP70x is dispensable for intraerythrocytic parasite growth at 37 {degree sign}C."

The trafficking block in Charnaud is likely due to a delay in parasite development and cannot thus really be directly related to PfEMP1 trafficking.

Charnaud et al., report: “Microscopy of Giemsa stained IE indicated that ΔHsp70-x appeared similar to CS2 with no obvious abnormalities (Fig 2c). To more accurately quantify changes in maturation through the cell cycle, the DNA content of parasites stained with ethidium bromide was measured by flow cytometry (Fig 2d). This indicated that most parasites had the same DNA content at each timepoint and were maturing at the same rate.”

Thus, we cannot conclude that the trafficking phenotype reported in the Charnaud study can be attributed to a growth delay. This is also supported by only minor changes in the transcriptome, which would likely be more widely perturbed if there was a significant growth delay. However, we will change the statement “Charnaud et al., found HSP70x to be essential for normal PfEMP1 trafficking”, to ”…important for PfEMP1 trafficking” to more precisely reflect the data.

(3) "NanoLuciferase (NanoLuc) fusion proteins and compartment-specific isolation confirmed a greater abundance of PfEMP1 in the RBC cytosol following heat stress."

Please see my comments about the differentiation between soluble and TM-containing proteins. One would expect that PfEMP1 is membrane-integrated, and thus should not be found in the cytosol (implying a soluble form).

See our response above.

(4) "Importantly, heat stress did not accelerate parasite development through the asexual life cycle (Supplementary Figure 1)."

The authors should constrain this statement to the time frame in which the heat-shock was given. Previous publications have shown a speeded-up development only in younger-stage parasites, which the authors did not study.

We will re-phrase.

Changes:

We have rephrased the sentence to clarify the time window of heat stress: ”Importantly, heat stress between 16-24 hours post-invasion did not accelerate parasite development through the asexual life cycle (Supplementary Figure 1).” The supplementary figure title has also been updated to match.

(5) I recommend that the authors include line numbers. This makes the reviewers' lives much easier.

We agree and apologize for this oversight.

We now added line numbers.

Reviewer #3 (Recommendations for the authors):

(1) All the experiments have been performed to a very high standard, and I have no major questions about the results. However, the paper would go up to the next level if the effect of fever temperatures on the stiffness of the iRBCs had been investigated by measuring the passage of iRBCs through an artificial spleen where a bed of metal spheres mimics interendothelial splenic slits.

See our comment from above.

(2) With respect to Figures 5E, 6C, and 6E, why was there not a decrease in bioluminescence levels at 39 {degree sign}C for Sap and NP40 to match the increase in EqtII?

The assay is not performed as a sequence of permeabilisation steps. Instead, samples are split into three parallel treatments: one with EqtII, one with Saponin, and one with NP40. The protein measured in each case reflects the total released under that specific condition rather than being cumulative. Therefore, the NP40 fraction includes proteins from the Saponin-accessible compartment, the EqtII-accessible compartment, and the parasite cytosol.

(3) In the Supplementary gene maps, I could not read the white text on the black gene boxes.

We apologize: these have not converted well and will be altered with the revised version.

Changes

We have significantly increased the size of all fonts within the gene maps and improved the resolution of the figures to improve readability.

(4) In Figure S6, why does HSP70-x look different between parts C and D IFAs, with the latter showing much more export?

We agree these IFAs are not optimal and we will provide better images.

New Results:

Immunofluorescence microscopy, including the localisation of the two HA-tagged proteins (PF3D7_1039000 and PF3D7_0702500), has been repeated and higher-quality images are now included in the updated manuscript (Supplementary Figures 9 and 11). These figures now include multiple images of HA-tagged staining to more accurately represent the observed localisation and export patterns.

(5) Would the authors care to comment on what kinase might be additionally phosphorylating at 39 {degree sign}C?

We presume these are Maurer’s clefts FIKK kinases as most of the hyperphosphorylated proteins are MC residents. However, without directly testing for this using conditional KO parasite lines, we cannot exclude that host kinases are also playing a role.

(6) Could the additional assembly of PSAC at the iRBC membrane be important for survival at 39 {degree sign}C?

We have tested to see if nutrient uptake helps parasite survival during heat stress in the presence of furosemide and lower nutrient concentrations, but did not see a difference in growth following heat stress compared to control temperature conditions.

New Results:

We have added a new supplementary figure (Supplementary Figure 4) detailing experiments testing parasite growth under altered nutrient availability using two approaches (sub-lethal furosemide concentrations or reduced-nutrient RPMI) and with or without a 40°C heat stress applied between 16-24 hpi.

The main text now references this data: “Culturing parasites in sub-lethal furosemide concentrations or in reduced nutrient media lead to reduced parasitaemia (Supplementary Figure 4). However, the parasitaemia is not further reduced following heat stress. This shows that increased PSAC levels/activity do not enhance parasite survival under conditions of limited nutrient availability either from furosemide-induced nutrient deprivation or a reduced nutrient media composition.”

These experiments show that nutrient uptake does not improve parasite survival during heat stress compared to control temperature conditions.

(7) Would the authors like to speculate on how higher temperatures increase the transport of exported proteins with TMDs?

There are many possible explanations, one of which is that unfolding of the hydrophobic TMD domains is favoured at elevated temperatures. However, we have no data to support this hypothesis and therefore refrained from particularly stating this possibility.

eLife Assessment

Du et al. present a valuable study examining neural activation in medial prefrontal cortex (mPFC) subpopulations projecting to the basolateral amygdala (BLA) and nucleus accumbens (NAc) during behavioral tasks assessing anxiety, social preference, and social dominance. The strength of the evidence linking in vivo neural physiology to behavioral outcomes was considered solid; however, the electrophysiology data and their interpretation were less well received. Overall, the reviewers felt that the revised work provides insight into how distinct mPFC→BLA and mPFC→NAc pathways influence anxiety, exploration, and social behaviors.

Reviewer #1 (Public review):

Summary:

It is well known that neurons in the medial prefrontal cortex (mPFC) are involved in higher cognitive functions such as executive planning, motivational processing and internal state mediated decision-making. These internal states often correlate with the emotional states of the brain. While several studies point to the role of mPFC in regulating behavior based on such emotional states, the diversity of information processing in its sub-populations remains a less explored territory. In this study, the authors try to address this gap by identifying and characterizing some of these sub-populations in mice using a combination of projection-specific imaging, function-based tagging of neurons, multiple behavioral assays and ex-vivo patch clamp recordings.

Strengths:

The authors targeted mPFC projections to the nucleus accumbens (NAc) and basolateral amygdala (BLA). Using the open field task (OFT), the authors identified four relevant behavioral states as well as neurons active while the animal was in the center region ("center-ON neurons"). By characterizing single unit activity and using dimensionality reduction, the authors show differentiated coding of behavioral events at both the projection and functional levels. They further substantiate this effect by showing higher sensitivity of mPFC-BLA center-ON neurons during time spent in the open arms of the elevated plus maze (EPM). The authors then pivoted to the three-chamber social interaction (SI) assay to show the different subsets of neurons encode preference of social stimulus over non-social. This reveals an interesting diversity in the function of these sub-populations on multiple levels. Lastly, the authors used the tube test as a manipulation of the anxiety state of mice and compared behavioral differences before/after in the OFT and social interaction tasks. This experiment revealed that "losers" of the tube test spend less time in the center of the open field while "winners" show a stronger preference for the familiar mouse over the object. Using patch-clamp experiments, the authors also found that "winners" exhibit stronger synaptic transmission in the mPFC-NAc projection while "losers" exhibit stronger synaptic transmission in the mPFC-BLA projection. Given the popularity of the tube test assay in rank determination, this provides useful insights into possible effects on anxiety levels and synaptic plasticity. Overall, the many experiments performed by the authors reveal interesting differences in mPFC neurons relative to their involvement in high or low anxiety behaviors, social preference and social rank.

Weaknesses:

The authors focused primarily on female mice limiting generalizability and leaving the readers with questions about the impact of sex differences on their results. The tube test is used as a manipulation of the "emotional state" in several of the experiments. While the authors show the changes to corticosterone levels as a consequence of win/loss in the tube test, stronger claims might be made with comparisons to other gold standard stressors such as forced social defeat or social isolation.

Reviewer #2 (Public review):

Summary:

The goal of this proposal was to understand how two separate projection neurons from the medial prefrontal cortex, those innervating the basolateral amygdala (BLA) and nucleus accumbens (NAc), contribute to the encoding of emotional behaviors. The authors record the activity of these different neuron classes across three different behavioral environments. They propose that, although both populations are involved in emotional behavior, the two populations have diverging activity patterns in certain contexts. A subset of projections to the NAc appear particularly important for social behavior. They then attempt to link these changes to the emotional state of the animal and changes in synaptic connectivity.

Strengths:

The behavioral data builds on previous studies of these projection neurons supporting distinct roles in behavior and extend upon previous work by looking at the heterogeneity within different projection neurons across contexts, this is important to understand the "neural code" within the PFC that contributes to such behaviours and how it is relayed to other brain structures.

Weaknesses:

The diversity of neurons mediating these projections and their targeting within the BLA and NAc is not explored. These are not homogeneous structures and so one possibility is that some of the diversity within their findings may relate to targeting of different sub-structures within BLA or NAc or the diversity of projection neuron subtypes that mediate these pathways. This is an important future direction for this work but does not detract from the main finding as reported. The electrophysiological data in Figure 7 have significant experimental confounds that makes their interpretation challenging.

Author Response:

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

Public review:

Reviewer #1 (Public review):

Weaknesses:

The authors focused primarily on female mice without commenting on the effect that sex differences would have on their results.

We agree that sex is an important biological variable. Our experiments were performed primarily in female mice to align with the higher prevalence of affective disorders in females and to maintain consistency across experiments. We now explicitly acknowledge this as a limitation in the Discussion and note that future studies will be needed to determine whether the projection-specific coding principles identified here generalize to male animals. Relevant literature on sex-specific mPFC→BLA/NAc function has also been incorporated.

While the authors have identified relevant behavioral states across the various behavioral tasks, there is still a missing link between them and "emotional states" - the phrase used by them emphatically throughout the manuscript. The authors have neither provided adequate references to satisfy this gap nor shared any data pertaining to relevant readouts such as cortisol levels.

We appreciate the reviewer’s concern regarding the use of the term “emotional states.” In the revised manuscript, we have clarified our terminology and now use “behavioral states associated with affective valence” where appropriate. We have also added references supporting the use of open field center vs. corner occupancy, elevated plus maze performance, and social interaction assays as established proxies for anxiety-like and affect-related behaviors.

Importantly, to provide physiological support for these interpretations, we now include data showing that repeated win/loss outcomes in the tube test are associated with increased corticosterone levels in loser mice. These results indicate that the behavioral manipulations used in this study are accompanied by measurable physiological changes linked to stress-related processes.

Both the projection-specific recordings and patch-clamp experiments, including histology reports in the manuscript, would provide essential information for anyone trying to replicate the results, especially since it's known that sub-populations in the BLA and NAc can have vastly different functions.

We agree that detailed reporting of projection targeting is important for reproducibility. We have expanded the Methods and Results to more clearly describe viral targeting, recording locations, and histological verification of mPFC projections to the lateral BLA and NAc shell. We also now explicitly acknowledge the anatomical and cellular heterogeneity within these regions as a limitation and discuss this as an important direction for future work.

The population-level analysis in the manuscript requires more rigor to reduce bias and statistical controls for establishing the significance of their results.

We have strengthened the statistical analyses throughout the manuscript. Specifically, we have incorporated permutation-based controls for key analyses, clarified how behavioral and neural features were defined, and provided additional details on dimensionality reduction and clustering approaches. Exact p values, sample sizes, and statistical tests are now reported throughout the manuscript and figure legends.

Lastly, the tube test is used as a manipulation of the "emotional state" in several of the experiments. While the tube test can cause a temporary spike in anxiety of the participating mice, it is not known to produce a sustained effect - unless there are additional interventions such as forced social defeat. Thus, additional controls for these experiments are essential to support claims based on changes in the emotional state of mice.

We agree that the tube test is not a classical chronic stress paradigm such as social defeat. In our study, the tube test was used to establish social hierarchy rather than to model sustained stress. We have revised the manuscript to clarify this point and have tempered our language accordingly. At the same time, our corticosterone measurements indicate that repeated social competition induces measurable physiological changes, suggesting that the paradigm captures aspects of social hierarchy–related stress. We now frame these effects conservatively and acknowledge the need for future studies using additional stress paradigms.

Apart from the methodology, the manuscript could also be improved with the addition of clear scatter points in all the plots along with detailed measures of the statistical tests such as exact p values and size of groups being compared.

We have revised all figures to include individual data points (scatter overlays) wherever appropriate and have improved reporting of statistical details, including exact p values and group sizes, to enhance transparency and reproducibility.

Taken together, these revisions clarify our interpretations, improve methodological transparency, and strengthen the rigor of the analyses while preserving the main conclusions of the study.

Reviewer #2 (Public Review):

Weaknesses:

The diversity of neurons mediating these projections and their targeting within the BLA and NAc is not explored. These are not homogeneous structures and so one possibility is that some of the diversity within their findings may relate to targeting of different sub-structures within each region.

We agree that both the basolateral amygdala (BLA) and nucleus accumbens (NAc) are highly heterogeneous. Our study was designed to focus on projection-defined mPFC outputs (presynaptic activity) rather than resolving postsynaptic subregional or cell-type diversity. We have now:

- Clarified targeting strategies (PL→NAc shell and PL→BLA basal region)

- Added histological descriptions of injection and recording sites

- Expanded the Discussion to acknowledge how subregional and cellular heterogeneity may contribute to the observed variability

We also highlight this as an important direction for future work.

The electrophysiological data have significant experimental confounds and more methodological information is required to support other conclusions related to these data.

We have significantly strengthened the electrophysiological component by:

- Providing detailed recording conditions (access resistance, membrane properties, inclusion criteria)

- Clarifying stimulus protocols and normalization procedures

- Including representative traces and quantification of exclusion rates

- Addressing potential confounds such as viral expression variability and stimulation parameters

These revisions improve both interpretability and reproducibility of the electrophysiological findings.

Reviewer #3 (Public Review):

Major Weaknesses:

(1) The manuscript does not clearly and consistently specify the sex of the mice used for behavioral and imaging experiments. Given the known influence of sex on emotional behaviors and neural activity, this omission raises concerns about the generalizability of the findings. The authors should make clear throughout the manuscript whether male, female, or mixed-sex cohorts were used and provide a rationale for their choice. If only one sex was used, the potential limitations of this approach should be explicitly discussed.

We agree that sex is an important biological variable. We have now clearly specified throughout the manuscript that experiments were performed primarily in female mice and have added a rationale for this choice in the Methods. Briefly, we focused on females to align with the higher prevalence of affective disorders in females and to maintain consistency across experiments. We now explicitly acknowledge this as a limitation in the Discussion and note that future studies will be needed to determine whether these findings generalize to male animals.

(2) Mice lacking "center-ON" neurons were excluded from analysis, yet the manuscript draws broad conclusions about the encoding of emotional states by mPFC pathways. It is critical to justify this exclusion and discuss how it may limit the generalizability of the findings. The inclusion of data or contextualization for animals without center-ON neurons would strengthen the interpretation.

We thank the reviewer for raising this important point. Mice lacking identifiable center-ON neurons were excluded from analyses that specifically relied on this functional classification, as inclusion of such datasets would preclude meaningful comparison of this neuronal population. We have now clarified this criterion in the Methods and Results. Importantly, this exclusion does not affect analyses performed at the population level or those not dependent on center-ON classification. We now explicitly discuss this limitation and note that variability in the presence of center-ON neurons may reflect biological heterogeneity across animals.

(3) The manuscript lacks baseline activity comparisons for mPFC→BLA and mPFC→NAc pathways across subjects. Providing baseline data would contextualize the observed activity changes during behavior testing and help rule out inter-individual variability as a confounding factor.

We have added baseline comparisons of mPFC→BLA and mPFC→NAc activity across subjects to control for inter-individual variability and better contextualize behavior-related changes.

(4) Extensive behavioral testing across multiple paradigms may introduce stress and fatigue in the animals, which could confound the induction of emotional states. The authors should describe the measures taken to minimize these effects (e.g., recovery periods, randomized testing order) and discuss their potential impact on the results.

We now provide detailed descriptions of experimental design, including habituation, randomized testing order, and recovery periods between assays. We also discuss potential cumulative stress effects as a limitation.

(5) Grooming is described as a "non-anxiety" behavior, which conflicts with its established role as a stress-relieving behavior that may indicate anxiety. This discrepancy requires clarification, as the distinction is central to the conclusions about the mPFC→BLA pathway's role in differentiating anxiety-related and non-anxiety behaviors.

We thank the reviewer for this important clarification. We agree that grooming can be associated with both stress-related and self-soothing behaviors. In the revised manuscript, we have clarified that grooming is not strictly a “non-anxiety” behavior but instead represents a distinct behavioral state that may reflect stress regulation or internal state transitions. We have revised the text accordingly to avoid oversimplification and to better align with the literature.

(6) While the study highlights pathway-specific neural activity, it lacks a cohesive integration of these findings with the behavioral data. Quantifying the overlap or decorrelation of neuronal activity patterns across tasks would solidify claims about the specialization of mPFC→NAc and mPFC→BLA pathways. Likewise, the discussion should be expanded to place these findings in light of prior studies that have probed the roles of these pathways in social/emotion/valence-related behaviors.

We agree that stronger integration between neural and behavioral findings would strengthen the manuscript. In the revised version, we have added quantitative analyses examining the similarity and divergence of activity patterns across behavioral contexts (e.g., cross-context comparisons and correlation-based analyses). We have also expanded the Discussion to better integrate our findings with prior studies on mPFC→NAc and mPFC→BLA pathways in reward, aversion, and social behavior, thereby providing a more cohesive interpretation of pathway-specific functions.

Minor Weaknesses:

(1) The manuscript does not explicitly state whether the same mice were used across all behavioral assays. This information is critical for evaluating the validity of group comparisons. Additionally, more detail on sample sizes per assay would improve the manuscript's transparency.

(2) In Figure 2G, the difference between BLA and NAc activity during exploratory behaviors (sniffing) is difficult to discern. Adjusting the scale or reformatting the figure would better illustrate the findings.

(3) While the characteristics of the first social stimulus (M1) are specified, there is no information about the second social stimulus (M2). This omission makes it difficult to fully interpret the findings from the three-chamber test.

(4) The methods section lacks detailed information about statistical approaches and animal selection criteria. Explicitly outlining these procedures would improve reproducibility and clarity.

We have addressed all these minor concerns, including:

- Clarifying whether the same mice were used across assays

- Reporting sample sizes for each experiment

- Improving figure clarity (e.g., scaling, labeling, scatter points)

- Providing details for social stimuli (M1 vs. M2)

- Expanding statistical methods and animal selection criteria

Summary

In summary, we have made substantial revisions to:

- Improve conceptual precision (behavior vs. emotional state)

- Increase methodological transparency and statistical rigor

- Strengthen physiological validation

- Clarify experimental design and limitations

- Enhance integration with existing literature

We believe these revisions significantly improve the clarity, rigor, and interpretability of the manuscript, and we are grateful for the reviewers’ guidance in strengthening this work.

eLife Assessment

This is a detailed and well-designed simulation study of the utility of replication metrics in animal-to-human study translations in bridging the gap between laboratory discoveries and health practice, a critical consideration in turning laboratory scientific research findings into tangible, real-world applications, to directly help human health. The study approaches are solid, and the findings are important, as they offer insights into clinical research translations to advance health decision-making. There is some potential for the strength and applicability of the presented evidence to be improved upon revision.

Reviewer #1 (Public review):

A well-designed and preregistered simulation study investigating whether replication-success metrics can be applied to assess animal-to-human translation. The study is comprehensive, uses realistic parameter settings, and provides valuable insights into how different metrics behave under varied conditions.

Strengths:

(1) Methodologically rigorous and transparently preregistered.

(2) Comprehensive simulation design covering a wide range of plausible scenarios.

(3) Clear description of metrics and decision rules.

(4) Valuable contribution to understanding the limitations of applying replication metrics to translation questions.

Weaknesses:

(1) The conceptual distinction between replication and translation could be more clearly emphasized.

(2) Interpretation of results is dense and can be challenging to follow without a clear and summarized.

(3) Some simulation parameters (effect sizes, heterogeneity, and number of animal studies) require more substantial justification.

(4) Practical recommendations could be more explicit to guide applied researchers.

Reviewer #2 (Public review):

Summary:

The authors attempt to address the issue of high rates of translation failure from animal studies to humans in the literature, where promising results in animal studies fail when conducting human clinical trials. Using parameters from a previous meta-analysis on prenatal amino acid supplementation and the effects it has on maternal blood pressure, the authors assessed the performance of the metrics used and whether they can quantify translation success. Performing a simulation study, the authors compared nine translation success metrics and found that no one method was uniformly optimal. The authors list several limitations of the study, such as comparability of effect sizes between animal and human studies, different goals of animal studies versus human studies, and the focus of the study on one aspect (statistics of translation) is part of a broader, more complex decision-making process before proceeding to human trials. The authors recommend using multiple metrics in combination while taking into consideration their strengths and weaknesses to assess the translation of animal studies to human outcomes. The paper achieves the aim of providing a model with several metrics to evaluate translation success from animal studies to humans.

Strengths:

(1) Utilizing 9 different translation success metrics in combination provides strong flexibility in evaluating whether results in animal studies can translate to humans. This would allow researchers to evaluate translation success using multiple different metrics according to the context of the study.

(2) The authors accommodated for the limited sample size in animal studies, which are typically underpowered, and also caution that special attention should be given to heterogeneity when interpreting translation results.

(3) Overall, this approach has the potential to be applied to other biomedical studies, provided the limitations for each of the metrics are considered. It would provide a useful tool in assessing translation from animals to humans, in addition to other factors such as safety, pharmacokinetics, etc.

Weaknesses:

While the study has several strengths, there are some limitations.

(1) Preclinical animal study sizes tend to be much smaller than human studies, which results in underpowered results. The authors adjusted for this by pooling animal study data. However, high heterogeneity in the animal studies can affect translation results.

(2) The study focuses only on evaluating the statistical component of translation, which is only one aspect of the decision-making process to move on to human trials. The study does not take into account safety and toxicological profiles, pharmacokinetics, or genetics, which are important considerations that influence the overall effect in humans.

Reviewer #3 (Public review):

Summary:

This paper focused on how to navigate the complex decision-making process of whether to go into human trials. This is a critical topic considering the well-documented challenges in replicating and translating findings. While these are two distinct topics (i.e., replication and translation), they are related, and the authors simulated many conditions to assess the utility of replication assessment metrics.

Strengths:

A major strength of the study is the detailed approach to identifying relevant conditions and metrics, and to providing rich results that outline the strengths and weaknesses of each metric. Any simulation study is challenged by trying to identify the most relevant variables of interest, and this study provided sound justification for its chosen variables of interest. While this study does not make a strong recommendation (which I see as a strength), it does provide a comprehensive overview of the various metrics and conditions that were investigated.

Weaknesses:

The weaknesses of the study are the limited focus on specific metrics, the assumptions, particularly in the limited number of human study variables, and the less-than-ideal approachable summary of findings for a non-technical audience.

Conclusion:

This paper provides a much-needed investigation and discussion of how decisions are made when assessing whether to go into human trials. This is an important topic that productively challenges the status quo, considering documented challenges in replication and translation in biomedical research.

eLife Assessment

The study investigates how CD1c-restricted T cells respond to Mtb-infected APCs, leading to increased cytokine production and cytotoxic activity that may help control Mtb infection. While the work is important and will interest researchers in the field, the supporting evidence is incomplete and could be strengthened by additional experiments. Experiments would: (i) evaluate THP1-CD1c cells to determine whether MHC surface expression is reduced or entirely abolished, (ii) enhance confidence in the purity of the CD1c-specific T cell population isolated from blood, and (iii) suggest what additional signal THP1-CD1c cells treated with Mtb express that is absent from the untreated cells.

Reviewer #1 (Public review):

Summary:

T cells that recognize lipids - CD1c - are frequent in circulation; however, their role in infection is unclear. This study aims to understand how Mtb infection can shape the responses of CD1c-specific T cells. CD1c is expressed in MTB granuloma, but in lower amounts than in nearby inflamed tissue. Mtb infection downregulates the expression of CD1c on monocyte-derived DCs. Single-cell RNA sequencing revealed the cytotoxic program inherent to the lipid-CD1c-specific T cells. Using an in vitro APC system where CD1c expression remains intact upon Mtb infection, the authors suggest that these T cells react better to Mtb-infected than uninfected Cd1c-expressing APC and reduce Mtb burden in infected cells. Therefore, Cd1c downregulation could be an immune evasion strategy used by Mtb.

Strengths:

This study asks an important question. The single-cell transcription analysis suggests the inherent cytotoxic program of lipid-CD1c cells and provides insights into their phenotypic and potential functional profiles. Function experiments suggest that these autoreactive T cells can react to Mtb infection, adding to the paradigm of infection control by these non-conventional T cell populations.

Weaknesses:

The study lacks sufficient rigor; conclusions may be strengthened with the incorporation of more controls, and some deeper characterization of the THP1 system and the CD1c-specific T cells isolated from blood. Crucial conclusions are drawn from the cell mixing experiments involving the engineered THP-1 system and CD1c-lipid-specific T cells from blood. These cells need more in-depth characterization. The expression of MHC-I/II is clearly reduced in THP1-CD1c cells. However, it is important to ensure that it is completely abolished, since a residual expression can skew the result with activation of conventional T cells in the blood or low levels of conventional T cells that may be present in the CD1c-tetra/multimer sorted T cells. CD1c-tetra/multimer sorting should include more markers than used in this study.

Figure 2: The immunohistochemistry appears to be shown only for one biopsy; it may be worth quantifying the immunohistochemistry of all five. The expression of CD1 molecules goes up during the differentiation of MoDC. And Mtb infection prevents or dampens the upregulation. Does Mtb infection downregulate the CD1 expression of mature DCs? Can the effect of Mtb on the expression of CD1a,b,c molecules be investigated using CD1c-expressing DCs from blood? What could be the reason THP-1 cells do not downregulate CD1 molecules upon Mtb infection, and how about the expression of CD1a and b?

Figure 3: (F) What does the X-axis read for the no infection group? The value for MOI = 0 should be incorporated for the infected T cell group.

Figure 4: In the lysis assay, THP1-CD1c cells (uninfected and infected) incubated alone should be incorporated.

Figure 5: A quantitative brief on the single cell TCR sequencing - including how many T cells were sequenced and the frequency of different clone including EM1 and EM2 - should be shown.

Reviewer #2 (Public review):

Summary:

The study by Milton et al titled "Human CD1c-autoreactive T cells recognise Mycobacterium tuberculosis-infected antigen-presenting cells and display cytotoxic effector programmes" characterises CD1c-restricted autoreactive T cells and their potential role in controlling Mtb infection. The authors develop a well-controlled system to assay for the functioning/activation of autoreactive T cells. They report the presence of CD1c-restricted autoreactive T cells in the circulating blood of healthy donors. They show that these T cells respond to CD1c and get activated even in the absence of any exogenous antigen. They next show that CD1c, along with CD1a and b, are typically downregulated on APCs during Mtb infection. These autoreactive T cells are cytotoxic, indicating they respond to Mtb treatment and/or to changes in the T cell ratio. The autoreactive T cells could effectively lyse Mtb-infected or PAMP-stimulated CD1c+APCs. Next, using TCR sequencing, they show that T cell responses were mediated by specific TCR clones with common sequence features. They show that these autoreactive T cells could curtail Mtb growth as measured by luminescence. Finally, using scRNAseq, they selectively identify the CD1c-reactive T cell pool and detect enrichment of typical effector memory CD4 and CD8 cells expressing cytolytic markers such as Granzyme, granulolysin, etc. The lung biopsy staining, along with the other data presented here, suggests that while CD1c-restricted T cells could have potential anti-bacterial roles, Mtb downregulation effectively shuts down this mechanism for TB control.

Strengths:

The study is designed well and has developed many exciting tools to generate specific information.

Weaknesses:

The study has weaknesses in two important parameters - novelty and relevance in controlling TB. Further, the results could be better presented and discussed to allow easy understanding of the experimental design. For example, at several places, UV-killed or live Mtb were used. What is the rationale behind that? Why use irradiated THP1-CD1c cells for activating T cells?

While functional assays identified only CD4+ cells as CD1c-restricted, scRNAseq shows that both CD4+ and CD8+ cells exhibit this phenotype. Identifying the specific lipid antigen presented by CD1c could add greater value to the study.

Since autoreactivity was independent of exogenous antigen, the cytotoxic activity should also be independent of exogeneous antigens? What additional signal a THP1-CD1c cells treated with UV-killed Mtb express that is absent from the untreated cells?

The relative Mtb growth assay is confusing. CD1c cells with Mtb infection triggers massive lytic response, as shown in Figure 4. Under similar conditions, in Figure 6, the authors report a significant decline in Mtb growth in these cells. The problem is that with the kind of lytic response observed, a lot more Mtb could be present extracellularly and would evade killing. How do we reconcile the two observations?

Reviewer #3 (Public review):

Summary:

Despite the rising global prevalence of TB, the role of non-classical T-cell pathways in host immunity remains unclear. The present study by Milton et al. is a novel contribution to the field of unconventional T-cell immunity in Mtb infection. The study addresses the role of CD1c-autoreactive T-cells and demonstrates that upon Mtb infection, these cells are significantly activated, resulting in increased cytokine production and cytotoxicity, and a reduction in the bacterial burden, specifically against Mtb-infected CD1c+ APCs (antigen-presenting cells). This defines their role as a plausible candidate for lipid-directed immunity in TB, complementary to MHC-restricted responses.

Strengths:

The manuscript is well written, and the novelty, impact, and limitations of this study are precisely highlighted by the authors.

Weaknesses:

The authors mention that they did not identify any specific lipids presented by CD1c on Mtb-infected APCs, making it unclear whether they are of host or bacterial origin. This leaves a gap in understanding why the response is enhanced in Mtb-infected cells, whether it is through altered self-presentation of lipids arising from Mtb-induced changes, infection-induced stress signals, or Mtb lipids, or through CD1c-dependent co-stimulation/infection signals. Direct lipid identification via lipidomics/MS of CD1c-bound lipids from Mtb-infected APCs would clarify whether the enhancement arises from altered self-lipids or subtle Mtb lipids.

eLife Assessment

This study provides valuable findings regarding potential correlates of protection against the African swine fever virus. The evidence supporting the claims is solid, and the results are highly relevant to the field. Further analysis using larger number of animals and other virus strains will help validate the importance of these findings and assess the relevance of the immune parameters associated with protection. The work will be of broad interest to veterinary immunologists, and particularly those working on African swine fever.

Reviewer #1 (Public review):

The study by Lotonin et al. investigates correlates of protection against African swine fever virus (ASFV) infection. The study is based on a comprehensive work, including the measurement of immune parameters using complementary methodologies. An important aspect of the work is the temporal analysis of the immune events, allowing to capture the dynamics of the immune responses induced after infection. Also, the work compares responses induced in farm and SPF pigs, showing the later an enhanced capacity to induce a protective immunity. Overall, the results obtained are interesting and relevant for the field. The findings described in the study further validate work form previous studies (critical role of virus-specific T cell responses), and provide new evidence on the importance of a balanced innate immune response during the immunization process. This information increases our knowledge on basic ASF immunology, one of the important gaps in ASF research that needs to be addressed for a more rational design of effective vaccines. As discussed in the manuscript, the results provide targets which can be further validated in other models, such as immunization using live attenuated vaccines.

Overall the conclusions of the work are well supported by the results, and most of the issues mentioned during the review have been properly addressed during the revision, improving the quality of the final manuscript. While some limitations remain, I consider that they do not invalidate the results obtained and are well discussed by the authors.

The study is highly relevant for the field, representing a step forward in our understanding of ASF protective immunity, providing immune targets to be further explored in other models and during vaccine development.

Reviewer #2 (Public review):

Summary:

In the current study the authors attempt to identify correlates of protection for improved outcomes following re-challenge with ASFV. An advantage is the study design which compares the responses to a vaccine like mild challenge and during a virulent challenge months later. It is a fairly thorough description of the immune status of animals in terms of T cell responses, antibody responses, cytokines and transcriptional responses and the methods appear largely standard. The comparison between SPF and farm animals is interesting and probably useful for the field in that it suggests that SPF conditions might not fully recapitulate immune protection in the real world. I thought some of the conclusions were over-stated and there are several locations where the data could be presented more clearly.

Strengths:

The study is fairly comprehensive in the depth of immune read-outs interrogated. The potential pathways are systematically explored. Comparison of farm animals and SPF animals gives insights into how baseline immune function can differ based on hygiene, which would also likely inform interpretation of vaccination studies going forward.

Weaknesses:

There are limited numbers of animals assessed.

Comments on revisions:

The authors mostly addressed my comments to the previous version. However, in the discussion they added comments relating to and an interpretation based on their own unpublished data and I think that those statements should be removed because the data are not included in this publication and cannot be cited.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The study by Lotonin et al. investigates correlates of protection against African swine fever virus (ASFV) infection. The study is based on a comprehensive work, including the measurement of immune parameters using complementary methodologies. An important aspect of the work is the temporal analysis of the immune events, allowing for the capture of the dynamics of the immune responses induced after infection. Also, the work compares responses induced in farm and SPF pigs, showing the latter an enhanced capacity to induce a protective immunity. Overall, the results obtained are interesting and relevant for the field. The findings described in the study further validate work from previous studies (critical role of virus-specific T cell responses) and provide new evidence on the importance of a balanced innate immune response during the immunization process. This information increases our knowledge on basic ASF immunology, one of the important gaps in ASF research that needs to be addressed for a more rational design of effective vaccines. Further studies will be required to corroborate that the results obtained based on the immunization of pigs by a not completely attenuated virus strain are also valid in other models, such as immunization using live attenuated vaccines.

While overall the conclusions of the work are well supported by the results, I consider that the following issues should be addressed to improve the interpretation of the results:

We thank Reviewer #1 for their thoughtful and constructive feedback, which significantly contributed to improving the clarity and quality of our manuscript. Below, we respond to each of the reviewer’s comments and describe the revisions that were incorporated.

(1) An important issue in the study is the characterization of the infection outcome observed upon Estonia 2014 inoculation. Infected pigs show a long period of viremia, which is not linked to clinical signs. Indeed, animals are recovered by 20 days post-infection (dpi), but virus levels in blood remain high until 141 dpi. This is uncommon for ASF acute infections and rather indicates a potential induction of a chronic infection. Have the authors analysed this possibility deeply? Are there lesions indicative of chronic ASF in infected pigs at 17 dpi (when they have sacrificed some animals) or, more importantly, at later time points? Does the virus persist in some tissues at late time points, once clinical signs are not observed? Has all this been tested in previous studies?

Tissue samples were tested for viral loads only at 17 dpi during the immunization phase, and long-term persistence of the virus in tissues has not been assessed in our previous studies. At 17 dpi, lesions were most prominently observed in the lymph nodes of both farm and SPF pigs. In a previous study using the Estonia 2014 strain (doi: 10.1371/journal.ppat.1010522), organs were analyzed at 28 dpi, and no pathological signs were detected. This finding calls into question the likelihood of chronic infection being induced by this strain.

(2) Virus loads post-Estonia infection significantly differ from whole blood and serum (Figure 1C), while they are very similar in the same samples post-challenge. Have the authors validated these results using methods to quantify infectious particles, such as Hemadsorption or Immunoperoxidase assays? This is important, since it would determine the duration of virus replication post-Estonia inoculation, which is a very relevant parameter of the model.

We did not perform virus titration but instead used qPCR as a sensitive and standardized method to assess viral genome loads. Although qPCR does not distinguish between infectious and non-infectious virus, it provides a reliable proxy for relative viral replication and clearance dynamics in this model. Unfortunately, no sample material remains from this experiment, but we agree that subsequent studies employing infectious virus quantification would be valuable for further refining our understanding of viral persistence and replication following Estonia 2014 infection.

(3) Related to the previous points, do the authors consider it expected that the induction of immunosuppressive mechanisms during such a prolonged virus persistence, as described in humans and mouse models? Have the authors analysed the presence of immunosuppressive mechanisms during the virus persistence phase (IL10, myeloid-derived suppressor cells)? Have the authors used T cell exhausting markers to immunophenotype ASFV Estonia-induced T cells?

We agree with the reviewer that the lack of long-term protection can be linked to immunosuppressive mechanisms, as demonstrated for genotype I strains (doi: 10.1128/JVI.00350-20). The proposed markers were not analyzed in this study but represent important targets for future investigation. We addressed this point in the discussion.

(4) A broader analysis of inflammatory mediators during the persistence phase would also be very informative. Is the presence of high VLs at late time points linked to a systemic inflammatory response? For instance, levels of IFNa are still higher at 11 dpi than at baseline, but they are not analysed at later time points.

While IFN-α levels remain elevated at 11 dpi, this response is typically transient in ASFV infection and likely not linked to persistent viremia. We agree that analyzing additional inflammatory markers at later time points would be valuable, and future studies should be designed to further understand viral persistence.

(5) The authors observed a correlation between IL1b in serum before challenge and protection. The authors also nicely discuss the potential role of this cytokine in promoting memory CD4 T cell functionality, as demonstrated in mice previously. However, the cells producing IL1b before ASFV challenge are not identified. Might it be linked to virus persistence in some organs? This important issue should be discussed in the manuscript.

We agree that identifying the cellular source of IL-1β prior to challenge is important, and this should be addressed in subsequent studies. We included a discussion on the potential link between elevated IL-1β levels and virus persistence in certain organs.

(6) The lack of non-immunized controls during the challenge makes the interpretation of the results difficult. Has this challenge dose been previously tested in pigs of the age to demonstrate its 100% lethality? Can the low percentage of protected farm pigs be due to a modulation of memory T and B cell development by the persistence of the virus, or might it be related to the duration of the immunity, which in this model is tested at a very late time point? Related to this, how has the challenge day been selected? Have the authors analysed ASFV Estonia-induced immune responses over time to select it?

In our previous study, intramuscular infection with ~3–6 × 10² TCID₅₀/mL led to 100% lethality (doi: 10.1371/journal.ppat.1010522), which is notably lower than the dose used in the present study, although the route here was oronasal. The modulation of memory responses could be more thoroughly assessed in future studies using exhaustion markers. The challenge time point was selected based on the clearance of the virus from blood and serum. We agree that the lack of protection in some animals is puzzling and warrants further investigation, particularly to assess the role of immune duration, potential T cell exhaustion caused by viral persistence, or other immunological factors that may influence protection. Based on our experience, vaccine virus persistence alone does not sufficiently explain the lack-of-protection phenomenon. We incorporated these important aspects into the revised discussion.

(7) Also, non-immunized controls at 0 dpc would help in the interpretation of the results from Figure 2C. Do the authors consider that the pig's age might influence the immune status (cytokine levels) at the time of challenge and thus the infection outcome?

We support the view that including non-immunized controls at 0 dpc would strengthen the interpretation of cytokine dynamics and will consider this in future experimental designs. Regarding age, while all animals were within a similar age range at the time of challenge, we acknowledge that age-related differences in immune status could influence baseline cytokine levels and infection outcomes, and this is an important factor to consider.

(8) Besides anti-CD2v antibodies, anti-C-type lectin antibodies can also inhibit hemadsorption (DOI: 10.1099/jgv.0.000024). Please correct the corresponding text in the results and discussion sections related to humoral responses as correlates of protection. Also, a more extended discussion on the controversial role of neutralizing antibodies (which have not been analysed in this study), or other functional mechanisms such as ADCC against ASFV would improve the discussion.

The relevant text in the Results and Discussion sections was revised accordingly, and the discussion was extended to more thoroughly address the roles of antibodies.

Reviewer #2 (Public review):

Summary:

In the current study, the authors attempt to identify correlates of protection for improved outcomes following re-challenge with ASFV. An advantage is the study design, which compares the responses to a vaccine-like mild challenge and during a virulent challenge months later. It is a fairly thorough description of the immune status of animals in terms of T cell responses, antibody responses, cytokines, and transcriptional responses, and the methods appear largely standard. The comparison between SPF and farm animals is interesting and probably useful for the field in that it suggests that SPF conditions might not fully recapitulate immune protection in the real world. I thought some of the conclusions were over-stated, and there are several locations where the data could be presented more clearly.

Strengths:

The study is fairly comprehensive in the depth of immune read-outs interrogated. The potential pathways are systematically explored. Comparison of farm animals and SPF animals gives insights into how baseline immune function can differ based on hygiene, which would also likely inform interpretation of vaccination studies going forward.

Weaknesses:

Some of the conclusions are over-interpreted and should be more robustly shown or toned down. There are also some issues with data presentation that need to be resolved and data that aren't provided that should be, like flow cytometry plots.

We appreciate the feedback from the Reviewer #2 and acknowledge the concerns raised regarding data presentation. In the revised manuscript, we clarified our conclusions where needed and ensured that interpretations were better aligned with the data shown.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In the Introduction, more details on the experimental model would be appreciated. A short summary of findings obtained with this model in previous works from the authors would help to better understand the context of the study.

Basic information on the model was added in the Introduction section of the revised manuscript.

(2) In Figure 1, the addition of more time points on the x-axes would help the interpretation of the figures.

We agree and have added extra time points to the x-axes.

(3) To better understand the results in Figure 2A, a figure showing cytokine levels post-Estonia infection of only challenged pigs would help, indicating protected and non-protected animals as in Figure 2C. This figure would be better linked to the corresponding dot plot (Figure 2B).

Our statistical analyses in Figure 2A are based on using both challenged and non-challenged pigs to assess differences between SPF and farm pigs. We prefer not to remove the non-challenged pigs in order to avoid losing statistical power. Moreover, even when non-challenged and challenged pigs are displayed in the plots, upregulation of IFN-α and IL-8 can be visualized and remains consistent with the positive and negative correlates of protection shown in Figure 2C.

(4) Dark red colour associated with SPF non-protected is difficult to differentiate from light red in some figures.

We thank the reviewer for this remark. To preserve the color scheme across the paper, we changed the circle data points to squares for the non-protected SPF pig in the most crowded figures: Figures 1–3 and Supplementary Figures 2 and 8.

(5) In Supplementary figures 12-16, grouping of the animal numbers (SPF vs farm) would facilitate the interpretation of the results.

Information on the animal numbers for each group (SPF vs. farm) has been added to the figure captions.

(6) Are the results shown in Figure 8 based on absolute scores as mentioned? Results from 0 dpc are not shown. Is that correct?

That is correct. BTM expression values are absolute and could not be normalized, as RNA was not isolated either immediately before the challenge or on day 0 post-challenge. This information is now clarified in the figure captions.

Reviewer #2 (Recommendations for the authors):

(1) The authors use the words "predicted" and "predicts" although they haven't used any methods to show that this is true, such as a multivariate analysis. I don't think correlation coefficients are sufficient to indicate prediction. This needs to be fixed.

We agree with this and have made changes in the text to avoid this impression.

(2) "Lower baseline immune activation was linked to increased protective immunity." Presumably, the authors mean prior to challenge, not prior to "vaccination"?

In this sentence written in the Abstract, we refer to baseline immune activation in the steady state, i.e., prior to any infection, as demonstrated in a previous study by Radulovic et al. (2022). The sentence was adapted accordingly. This concept is further explored in the Discussion section.

(3) The abstract mentioned the comparison between farm and SPF pigs, but didn't provide any context for those findings. It could be added here.

In the new version, we have added information on this model in the Introduction section.

(4) Figure legends need N to be indicated. For example, the viral load figures don't appear to be representative of all 9 or 5 animals. Is there a reason why not all were challenged, and how were those 5 challenged selected?

Numbers of animals in each group were added to the figure captions. We have also provided details regarding the animals sacrificed at different time points of the experiment in the ‘Animal experiment’ section of the Methods.

(5) 1A doesn't have a legend to indicate whether dark or light color indicates sampling.

Fair point. We have added the information to the figure.

(6) For Figure 3C, it's not clear how the correlation is presented. The legend indicates in writing that the color indicates the outcome it correlates with, but the legend suggests that it is r.

The method of presenting correlation data is consistent across all figures, including Figure 3C. The color reflects the direction and strength of the correlation, corresponding to the r coefficient obtained from correlating immunological parameters with clinical scores. We have clarified this description in the figure caption to improve readability.

(7) For some of the correlation data in 2D and 3C, it would be nice to provide the plots in the supplemental. Also, are there enough data points for a robust interpretation of correlation curves?

We agree that providing the plots will improve clarity and have included them in the supplementary material. While we acknowledge that the number of data points is modest, we believe it is sufficient to support a robust interpretation of the correlation curves. Corresponding p-value cutoffs are noted in the figure captions.

(8) The figure 2C method of indicating significance is confusing. There must be a clearer way to present this figure.

Analyzing statistical significance for the dataset shown in Figure 2C is challenging due to the small number of animals. We carefully considered alternative ways of presenting statistical significance, however, given the limited group sizes, we believe that the current approach provides the most transparent and informative representation of the data.

For clarity, we divided the animals into SPF and farm groups, as well as into protected (4 SPF, 2 farm pigs) and non-protected (1 SPF, 3 farm pigs) categories, and performed both group-based (unpaired t-test) and time-based (mixed-effects analysis) comparisons. All significant differences were added to the plots so that readers could directly visualize the observed trends and compare them with the correlation analysis presented in Figure 2D.

(9) Please note that "viremia" means the presence of a virus specifically in the blood. Other descriptions of viral load should be used if this was not measured.

We have clarified this in the text. When referring to organs, we use the term “viral loads.”

(10) The way of putting a square around boxes that are significant can be misleading when a box is surrounded by other significant comparisons. Like for Figure 6B - probably all of these are really significant, but I can't tell for sure.

Good point. We changed rectangles to circles for better readability of the figures.

(11) There is a potential argument that these correlates of protection might only be valid for this specific vaccine. It should be noted that comparisons of multiple vaccines would be needed before assuming the correlates are broadly relevant.

We agree with this statement and address it in the Discussion section.

(12) For the circled pathways in Figure 9, it is not clear from the diagram if there is a directionality to the involvement of those pathways. Modulated or induced?

When discussing pathways identified by transcriptome analysis, we are always referring to their induction, as this is based on the normalized enrichment score (NES). We have now specified this in the figure caption.

(13) The authors speculate about NK cells, but this is based on transcriptional pathways identified and the literature. Is there any indication from the flow cytometry data whether activated NK cells versus NKT cells are associated with protection? Also, the memory phenotype of those cells?

Regarding NK cells, the BTM analysis was corroborated by the flow cytometry data shown in Supplementary Figure 8. NK cells were defined as CD3^-CD8α⁺. Specific markers to distinguish NKT cells or to assess memory phenotypes were not included in our panel.

(14) In the discussion, "Our study demonstrates that T cell activation represents a robust correlate of protection against ASFV" doesn't indicate whether they mean after vaccination or after challenge. Re-using the same time points throughout the manuscript compounds this confusion.

In this case, we mean that T cell activation upon immunization/vaccination and challenge correlates with protection. This information has been added to the sentence. Although some time points overlap between the immunization and challenge phases, we consistently use “dpi” and “dpc” to clearly distinguish them.

(15) Flow cytometry gating strategies should be provided in the supplemental, particularly since this species is less frequently studied using flow cytometry; it would be helpful to understand gating and expression levels of key markers.

We have provided the gating strategy in Supplementary Figure 7, which is also referenced in the “Flow cytometry and hematology analysis” section of the Methods.

(16) Some of the discussion is a bit long and repetitive - e.g. the parts on antibodies and the last paragraph with multiple other parts of the discussion and manuscript.

While we agree that some sections are extensive, we think that this level of detail is necessary to integrate the different datasets and to place our findings in the context of previous literature.

eLife Assessment

This study provides an important contribution by showing that whiteflies and planthoppers use salivary effectors to suppress plant immunity through the receptor-like protein RLP4, suggesting convergent evolution in these insect lineages. The topic is of clear interest for understanding plant-insect interactions and offers ideas that could stimulate further research in the field. The authors provide convincing evidence for the functional roles of the salivary effectors.

Reviewer #1 (Public review):

Summary:

This manuscript investigates how herbivorous insects, specifically whiteflies and planthoppers, utilize salivary effectors to overcome plant immunity by targeting the RLP4 receptor.

Strengths:

The authors present a strong case for the independent evolution of these effectors and provide compelling evidence for their functional roles.

Comments on revisions:

The authors have addressed all my concerns.

Reviewer #2 (Public review):

Summary:

The authors tested an interesting hypothesis that white flies and planthoppers independently evolved salivary proteins to dampen plant immunity by targeting a receptor like protein. Unlike previously reported receptor like proteins with large ligand-binding domains, the NtRLP4 here has a malectin LRR domain. Interestingly, it also associates with the adaptor SOBIR1. While the function of this protein remains to be further explored, the authors provide strong evidence showing it's the target of salivary proteins as the insects' survival strategy.

The authors have nicely addressed the questions I raised.

I noticed two small points the authors may modify:<br /> - Line 16: delete "on"<br /> - Line 185: Replace "is resistant to B. tabaci infestation" with "confers resistance against B. tabaci".

Reviewer #3 (Public review):

Summary:

In this study, Wang et al., investigates how herbivorous insects overcome plant receptor-mediated immunity by targeting plant receptor-like proteins. The authors identify two independently evolved salivary effectors, BtRDP in whiteflies and NlSP694 in brown planthoppers, that promote the degradation of plant RLP4 through the ubiquitin-dependent proteasome pathway.

Strengths:

This work highlights a convergent evolutionary strategy in distinct insect lineages and advances our understanding of insect-plant coevolution at the molecular level.

Comments on revisions:

The authors have satisfactorily addressed all the issues I raised.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript investigates how herbivorous insects, specifically whiteflies and planthoppers, utilize salivary effectors to overcome plant immunity by targeting the RLP4 receptor.

Thank you for your comments.

Strengths:

The authors present a strong case for the independent evolution of these effectors and provide compelling evidence for their functional roles.

Thank you for your help in improving our manuscript

Reviewer #2 (Public review):

Summary:

The authors tested an interesting hypothesis that white flies and planthoppers independently evolved salivary proteins to dampen plant immunity by targeting a receptor-like protein. Unlike previously reported receptor-like proteins with large ligand-binding domains, the NtRLP4 here has a malectin LRR domain. Interestingly, it also associates with the adaptor SOBIR1. While the function of this protein remains to be further explored, the authors provide strong evidence showing it's the target of salivary proteins as the insects' survival strategy.

Thank you for your comments.

Major points:

The authors mixed the concepts of LRR-RLPs with malectin LRR-RLPs. These are two different type of receptors. While LRR-RLPs are well studied, little is known about malectin LRR-RLPs. The authors should not simply apply the mode of function of LRR-RLPs to RLP4 which is a malectin LRR-RLP. In addition, LRR-RLPs that function as ligand-binding receptors typically possess >20 LRRs, whereas RLP4 in this work has a rather small ectodomain. It remains unclear whether it will function as a PRR. I can't agree with the author's logic of testing uninfested plants for proving a PRR's function. The function of a pattern recognition receptor depends on perceiving the corresponding ligand. As shown by the data provided, RLP4-OE plants have altered transcriptional profile indicating activated defense, suggesting it's unlikely a PRR. An alternative explanation is needed. More work on BAK1 will also help to clarify the ideas proposed by the authors.

We sincerely thank the reviewer for the insightful and constructive comments, which have helped us critically re-evaluate our interpretation of RLP4 function. In the revised manuscript, we have addressed this important point by adding a detailed discussion of an alternative explanation for RLP4’s role in plant defense. Specifically, we now explicitly distinguish between classical LRR-RLPs and malectin-domain-containing RLPs, and we acknowledge that RLP4 may not function as a canonical PRR. We also discuss the structural features of RLP4, including its malectin-like domain and relatively small LRR region, and the observation that NtRLP4 overexpression lines exhibit altered transcriptional profiles even in the absence of insect infestation. Based on these lines of evidence, we propose that RLP4 may instead act as a regulatory component within plant immune signaling networks, modulating defense outputs rather than functioning as a direct ligand receptor. The revised discussion now reads as follows: “Together, this study reveals that suppressing PRR-mediated plant immunity may be a conserved strategy employed by herbivorous insects for successful feeding. We demonstrate that whiteflies and planthoppers have independently evolved salivary effectors that facilitate the ubiquitin-dependent degradation of defensive RLP4 in host plants, thereby dampen RLP4-mediated plant immunity (Fig. 6). Nevertheless, the precise mechanism by which RLP4 contributes to plant defense warrants further consideration. While it may function as a canonical PRR that perceives insect-derived molecular patterns, several lines of evidence point to an alternative interpretation. Structurally, RLP4 differs from classical LRR-RLP: it contains a malectin-like domain and a relatively small LRR domain, contrasting with typical LRR-RLPs that often possess large LRRs dedicated to ligand binding. Functionally, NtRLP4 overexpression lines exhibit significantly altered transcriptional profiles and dysregulated SA/JA pathways even in the absence of insect infestation, a phenotype inconsistent with canonical PRRs, which typically remain quiescent until ligand perception. These findings point to an alternative explanation: rather than functioning as a classical PRR that recognizes insect-derived molecules, RLP4 may act as a regulatory component within plant immune signaling networks. Elucidating the precise mechanism of RLP4 in conferring plant defense against herbivorous insects will therefore be an important focus of future research” in Line 392-407.

Reviewer #3 (Public review):

Summary:

In this study, Wang et al., investigate how herbivorous insects overcome plant receptor-mediated immunity by targeting plant receptor-like proteins. The authors identify two independently evolved salivary effectors, BtRDP in whiteflies and NlSP694 in brown planthoppers, that promote the degradation of plant RLP4 through the ubiquitin-dependent proteasome pathway. NtRLP4 from tobacco and OsRLP4 from rice are shown to confer resistance against herbivores by activating defense signaling, while BtRDP and NlSP694 suppress these defenses by destabilizing RLP4 proteins.

Thank you for your comments.

Strengths:

This work highlights a convergent evolutionary strategy in distinct insect lineages and advances our understanding of insect-plant coevolution at the molecular level.

Two minor comments:

In line 140, yeast two-hybrid (Y2H) was used to screen for interacting proteins in plants. However, it is generally difficult to identify membrane receptors using Y2H. Please provide more methodological details to justify this approach, or alternatively, include a discussion explaining this.

Thank you for pointing this out. It is true that Y2H is generally difficult to identify membrane receptors. To address this limitation, we used truncated versions of RLP4s lacking the signal peptide and transmembrane domains in point-to-point Y2H assays. In addition, the interactions between BtRDP and RLP4s were further validated by Co-IP and BiFC experiments. In the revised manuscript, we have clarified this methodological detail as follows: “Given that Y2H is generally difficult to identify membrane receptors, the truncated versions of NtRLP4/SlRLP4/OsRLP4 lacking the signal peptide and transmembrane domains were used” in Linr 636-638.

In Figure S12C, the interaction between the two proteins appears to be present in the nucleus as well. Please provide a possible explanation for this observation.

Thank you for pointing this out. During revision, we further examined the subcellular localization of NtRLP4 and found that NtRLP4-GFP could also be detected in the nucleus when expressed alone (Fig. S18), suggesting that NtRLP4 may have additional functions beyond serving as a cell surface pattern recognition receptor. In the revised manuscript, we discussed that NtRLP4 might play other roles in addition to PRRs in the discussion section as follow: “Together, this study reveals that suppressing PRR-mediated plant immunity may be a conserved strategy employed by herbivorous insects for successful feeding. We demonstrate that whiteflies and planthoppers have independently evolved salivary effectors that facilitate the ubiquitin-dependent degradation of defensive RLP4 in host plants, thereby dampen RLP4-mediated plant immunity (Fig. 6). Nevertheless, the precise mechanism by which RLP4 contributes to plant defense warrants further consideration. While it may function as a canonical PRR that perceives insect-derived molecular patterns, several lines of evidence point to an alternative interpretation. Structurally, RLP4 differs from classical LRR-RLP: it contains a malectin-like domain and a relatively small LRR domain, contrasting with typical LRR-RLPs that often possess large LRRs dedicated to ligand binding. Functionally, NtRLP4 overexpression lines exhibit significantly altered transcriptional profiles and dysregulated SA/JA pathways even in the absence of insect infestation, a phenotype inconsistent with canonical PRRs, which typically remain quiescent until ligand perception. These findings point to an alternative explanation: rather than functioning as a classical PRR that recognizes insect-derived molecules, RLP4 may act as a regulatory component within plant immune signaling networks. Elucidating the precise mechanism of RLP4 in conferring plant defense against herbivorous insects will therefore be an important focus of future research” in Line 392-407.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have addressed all my concerns.

Thank you for your help in improving our manuscript

Reviewer #2 (Recommendations for the authors):

This work is quite interesting. It's not necessary to prove RLP4 as a PRR to show the merit of this discovery. The current logic is forced and thus the conclusion not convincing. Finding an alternative explanation will be more helpful.

Thank you for your valuable suggestions. In the revised version, we discussed the alternative explanation as follow: “Together, this study reveals that suppressing PRR-mediated plant immunity may be a conserved strategy employed by herbivorous insects for successful feeding. We demonstrate that whiteflies and planthoppers have independently evolved salivary effectors that facilitate the ubiquitin-dependent degradation of defensive RLP4 in host plants, thereby dampen RLP4-mediated plant immunity (Fig. 6). Nevertheless, the precise mechanism by which RLP4 contributes to plant defense warrants further consideration. While it may function as a canonical PRR that perceives insect-derived molecular patterns, several lines of evidence point to an alternative interpretation. Structurally, RLP4 differs from classical LRR-RLP: it contains a malectin-like domain and a relatively small LRR domain, contrasting with typical LRR-RLPs that often possess large LRRs dedicated to ligand binding. Functionally, NtRLP4 overexpression lines exhibit significantly altered transcriptional profiles and dysregulated SA/JA pathways even in the absence of insect infestation, a phenotype inconsistent with canonical PRRs, which typically remain quiescent until ligand perception. These findings point to an alternative explanation: rather than functioning as a classical PRR that recognizes insect-derived molecules, RLP4 may act as a regulatory component within plant immune signaling networks. Elucidating the precise mechanism of RLP4 in conferring plant defense against herbivorous insects will therefore be an important focus of future research” in Line 392-407.

Inappropriate descriptions still exist at multiple places across the manuscript and damages the merit of this work. I highly recommend the authors to consult an expert in plant PRR research for proof reading. The language editing service the authors used only provided limited help in this case. Here are a few examples:

We sincerely thank the reviewer for the critical and constructive comments. We agree that precise language is essential for conveying scientific findings. In the revised version, we have refined the text with the help of colleagues who have expertise in plant immunity, aiming to ensure the descriptions are as precise and professional as possible.

Line 16: Using "depend" ignores the fact that many biotic invaders are recognized by NLRs. The authors can simply use the word "use" or "utilize".

Thank you for your suggestion. We corrected it in the revised version.

Line 20:"target defensive RLP4, therefor minimizing the plant immunity" is a strange saying. "dampen RLP4-mediated plant immunity"will be better.

Thank you for your suggestion. We corrected it in the revised version.

Line 49: as far as I know, only LRR-RLPs use SOBIR1 as adaptor. The authors should introduce this specific point. The mode of action of other type of LRR-RLPs are less clear.

Thank you for your suggestion. In the revised version, we re-introduce this as follow: “As RLPs lack the intracellular signaling domains, they are anticipated to associate with adaptor kinases to form the bimolecular receptor kinases. For example, suppressor of BAK1-interacting receptor-like kinase 1 (SOBIR1) is reported to act as a common adaptor for most, if not all, of the leucine-rich repeat RLP (LRR-RLP)” in Line 48-52, “The receptor-like kinase SOBIR1, which contained a kinase domain, has been widely reported to be required for the function of LRR-RLPs in the innate immunity. However, whether SOBIR1 interacted with malectin-LRR RLP remains largely unknown” in Line 170-173.

Line 67: There are quite a few publications showing that insect salivary proteins dampen plant immunity.

Sorry for the inaccurate description. We agree that an accumulated literature describes the suppression of plant immunity by insect salivary proteins. However, the specific molecular mechanism by which these proteins target plant PRRs is still poorly understood. In the revised version, we specified that “it remains largely unknown how insects cope with plant PRRs” in Line 68-69.

Line 149: I don't understand what "point-to-point Y2H" is.

Thank you for your comment. We agree that the term "pairwise Y2H" is more commonly used in the literature than "point-to-point Y2H." To avoid any confusion and to align with standard terminology, we have replaced "point-to-point Y2H" with "pairwise Y2H" throughout the revised manuscript.

Line 179: Replace with "NtRLP4 and NtSOBIR1 confers resistance to B. tabaci". You don't say a protein is resistant to a insect infestation. The same applies for Line 209-210.

Thank you for your suggestion. We corrected it in the revised version.

Minor points:

Line 91-92: Lengthy text for simple results.

Line 98: "which was significantly different from the actin or ribosomal 18S rRNA" can be deleted. It's self-evident that actin and 18S rRNA are controls. The same applies to Line 101.

Line 130: unnecessary sentence, delete.

The use of verb forms needs further correction.

Thank you for your valuable suggestion. In the revised manuscript, we have revised the text accordingly. We truly appreciate your help in improving our manuscript.

eLife Assessment

This study uses a Bayesian framework to characterize latent brain state dynamics associated with memory encoding and performance in children, as measured with functional magnetic resonance imaging. The novelty of the approach offers valuable insights into memory-related brain activity, but the consideration of developmental changes in memory and brain dynamics, and the evidence to support the proposed mapping between specific states and distinct aspects of memory, are incomplete. This work will be of interest to researchers interested in cognitive neuroscience and the development of memory.

Reviewer #1 (Public review):

Summary:

Zeng et al. characterized the dynamic brain states that emerged during episodic encoding and the reactivation of these states during the offline rest period in children aged 8-13. In the study, participants encoded scene images during fMRI and later performed a memory recognition test. The authors adopted the BSDS approach and identified four states during encoding, including an "active-encoding" state. The occupancy rate of, and the state transition rates towards, this active-encoding state positively predicted memory accuracy across participants. The authors then decoded the brain states during pre- and post-encoding rests with the model trained on the encoding data to examine state reactivation. They found that the state temporal profile and transition structure shifted from encoding to post-encoding rest. They also showed that the mean lifetime and stability (measured with self-transition probability) of the "default-mode" state during post-encoding rest predict memory performance.

Strengths:

How brain dynamics during encoding and offline rest support long-term memory remains understudied, particularly in children. Thus, this study addresses an important question in the field. The authors implemented an advanced computational framework to identify latent brain states during encoding and carefully characterized their spatiotemporal features. The study also showed evidence for the behavioral relevance of these states, providing valuable insights into the link between state dynamics and successful encoding and consolidation.

Weaknesses:

(1) If applicable, please provide information on the decoding performance of states during pre- and post-encoding rests. The Methods noted that the authors applied a threshold of 0.1 z-scored likelihood, and based on Figure S2, it seems like most TRs were assigned a reinstated state during post-encoding rest. It would be useful to know, for the decodable TRs, how strong the evidence was in favor of one state over others. Further, was decoding performance better during post- vs. pre- encoding rest? This is critical for establishing that these states were indeed "reinstated" during rest. The authors showed individual-specific correlations between encoding and post-encoding state distribution, which is an important validation of the method, but this result alone is not sufficient to suggest that the states during encoding were the ones that occurred during rest. The authors found that the state dynamics vary substantially between encoding and rest, and it would be helpful to clarify whether these differences might be related to decoding performance. I am also curious whether, if the authors apply the BSDS approach to independently identify brain states during rest periods (instead of using the trained model from encoding), they find similar states during rest as those that emerged during encoding?

(2) During post-encoding rest, the intermediate activation state (S1) became the dominant state. Overall, the paper did not focus too much on this state. For example, when examining the relationship between state transitions and memory performance, the authors also did not include this state as a part of the analyses presented in the paper (lines 203-211). Could the author report more information about this state and/or discuss how this state might be relevant to memory formation and consolidation?

(3) Two outcome measures from the BSDS model were the occupancy rate and the mean lifetime. The authors found a significant association with behavior and occupancy rate in some analyses, and mean lifetime in others. The paper would benefit from a stronger theoretical framing explaining how and why these two different measures provide distinct information about the brain dynamics, which will help clarify the interpretation of results when association with behavior was specific to one measure.

(4) For performance on a memory recognition test, d' is a more common metric in the literature as it isolates the memory signal for the old items from response bias. According to Methods (line 451), the authors have computed a different metric as their primary behavioral measure (hits + correction rejections - misses - false alarms). Please provide a rationale for choosing this measure instead. Have the authors considered computing d' as well and examining brain-behavior relationships using d'?

(5) While this study examined brain state dynamics in children, there was no adult sample to compare with. Therefore, it is hard to conclude whether the findings are specific to children (or developing brains). It would be helpful to discuss this point in the paper.

Reviewer #2 (Public review):

This paper investigates the latent dynamic brain states that emerge during memory encoding and predict later memory performance in children (N = 24, ages: 8 -13 years). A novel computational approach (Bayesian Switching Dynamic Systems, BSDS) discovers latent brain states from fMRI data in an unsupervised and parameter-free manner that is agnostic to external stimuli, resulting in 4 states: an active-encoding state, a default-mode state, an inactive state, and an intermediate state. The key finding is that the percentage of time occupied in the active-encoding state (characterized by greater activity in hippocampal, visual, and frontoparietal regions), as well as greater transitions to this state, predicts memory accuracy. Memory accuracy was also predicted by the mean lifetime and transitions to the default-mode state (characterized by greater activity in medial prefrontal cortex and posterior cingulate cortex) during post-encoding rest. Together, the results provide insights into dynamic interactions between brain regions that may be optimal for encoding novel information and consolidating memories for long-term retention.

The approach is interesting and important for our understanding of neural mechanisms of memory during development, as we know less about dynamic interactions between memory systems in development.

Moreover, the novel methodology may be broadly useful beyond the questions addressed in this study. The manuscript is well-written and concise. Nonetheless, there are several areas for improvement:

(1) The study focuses on middle childhood, but there is a lack of engagement in the Introduction or Discussion about what is known about memory development and the brain during this period. Many of the brain regions examined in this study, particularly frontoparietal regions, undergo developmental changes that could influence their involvement in memory encoding and consolidation. The paper would be strengthened by more directly linking the findings to what is already known about episodic memory development and the brain.

(2) A more thorough overview of the BSDS algorithm is needed, since this is likely a novel method for most readers. Although many of the nitty-gritty details can be referenced in prior work, it was unclear from the main text if the BSDS algorithm discovered latent states based on activation patterns, functional connectivity, or both. Figure 1F is not very informative (and is missing labels).

(3) A further confusion about the BSDS algorithm was whether it necessarily had to work on the rest data. Figure 4A suggests that each TR was assigned one of the four states based on the maximum win from the log-likelihood estimation. Without more details about how this algorithm was applied to the rest data, it is difficult to evaluate the claim on page 14 about the spontaneous emergence of the states at rest.

(4) Although the BSDS algorithm was validated in prior simulations and task-based fMRI using sustained block designs in adults, it is unclear whether it is appropriate for the kind of event-related design used in the current study. Figure 1G shows very rapid state changes, which is quantified in the low mean lifetime of the states (between 1-3 TRs on average) in Figure 4C. On the one hand, it is a strength of the algorithm that it is not necessarily tied to external stimuli. On the other hand, it would be helpful to see simulations validating that rapid transitions between states in fMRI data are meaningful and not due to noise.

(5) The Methods section mentions that participants actively imagined themselves within the encoded scenes and were instructed to memorize the images for a later test during the post-encoding rest scan. This detail needs to be included in the main text and incorporated into the interpretation of the findings, as there are likely mechanistic differences between spontaneous memory replay/reinstatement vs. active rehearsal.

(6) Information about the general linear model used to discover the 16 ROIs that showed a subsequent memory effect are missing, such as: covariates in the model (motion, etc.), group analysis approach (parametric or nonparametric), whether and how multiple-comparisons correction was performed, if clusters were overlapping at all or distinct, if the total number of clusters was 16 or if this was only a subset of regions that showed the effect.

Reviewer #3 (Public review):

Summary:

This paper uses a novel method to look at how stable brain states and the transitions between them promote memory formation during encoding and post-encoding rest in children. I think the paper has some weaknesses (detailed below) that mean that the authors fall short of achieving their aims. Although the paper has an interesting methodological approach, the authors need better logic, and are potentially "double dipping" in their results - meaning their logic is circular. I think the method that they are using could be useful to the broader neuroimaging community, although they need to make this argument clearer in the paper.

Strengths:

The paper is interesting in that they use a novel method to look at brain state dynamics and how they might support memory.

Weaknesses:

The paper has several weaknesses:

(1) The authors use children as their study subjects but fail to reconcile why children are used, if the same phenomena are expected to be seen in adults (or only children), and if and how their findings change with age across an age range that ranges from middle childhood into early adolescence. They need to include more consideration for the development of their subject population. The authors should make it clear why and how memory was tested in children and not adults. Are adults and children expected to encode and consolidate in a similar manner to children? Do the findings here also apply to adults? Do the findings here also apply to adults? How was the age range of 8-13-year-old children selected? Why didn't the authors look at change with age? Does memory performance change with age? Do the BSDS dynamics change with age in the authors' sample?

(2) The authors look for brain state dynamics within a preselected set of ROIs that are selected because they display a subsequent memory effect. This is problematic because the state that is most associated with subsequent memory (S3, or State 3) is also the one that shows most activity in these regions (that have already been a priori selected due to displaying a subsequent memory effect). This logic is circular. It would be helpful if they could look at brain state dynamics in a more ROI agnostic whole brain approach so that we can learn something beyond what a subsequent memory analysis tells us. I think the authors are "double dipping" in that they selected regions for further analysis based on a subsequent memory association (remembered > forgotten contrast) and then found states within those regions showing a subsequent memory effect to further analyze for being associated with subsequent memory. Would it be possible instead to do a whole-brain analysis (something a bit more agnostic to findings) using the BSDS framework, and then, from a whole-brain perspective, look for particular brain states associated with subsequent memory? As it stands, it looks like S3 (state 3) has greater overall activation in all brain regions associated with subsequent memory, so it makes sense that this brain state is also most associated with subsequent memory. The BSDS analysis is therefore not adding anything new beyond what the authors find with the simple subsequent memory contrast that they show in Figure 1C. This particularly effects the following findings: (a) active-encoding state occupancy rate correlated positively with memory accuracy, (b) transitions to the active-encoding state were beneficial / Conversely, transitions toward the inactive state (S4) were detrimental, with incoming transitions showing negative correlations with memory accuracy / The active-encoding state serves as a "hub" configuration that facilitates memory formation, while pathways leading to this state enhance performance and transitions away from it impair encoding.

(3) The task used to test memory in children seems strange. Why should children remember arbitrary scenes? How this was chosen for encoding needs to be made clear. There needs to be more description of the memory task and why it was chosen. Why was scene encoding chosen? What does scene encoding have to do with the stated goal of (a) "Understanding how children's brains form lasting memories", (b) "optimizing education" and (c) "identifying learning disabilities"? What was the design of the recognition memory test? How many novel scenes were included in the test, and how were they chosen? How close were the "new" images to previously seen "old" images? Was this varied parametrically (i.e., was the similarity between new and old images assessed and quantified?)

(4) They ultimately found four brain states during encoding. It would be helpful if they could make the logic and foundation for arriving at this number clear.

(5) There is already extant work on whether brain states during post-encoding rest predict memory outcomes. This work needs to be cited and referred to. The present manuscript needs to be better situated within prior work. The authors should look at the work by Alexa Tompary and Lila Davachi. They have already addressed many of the questions that the authors seek to answer. The authors should read their papers (and the papers they cite and that cite them) and then situate their work within the prior literature.

More minor weaknesses:

(1) The authors should back up the claim that "successful episodic memory formation critically depends on the temporal coordination between these systems. Brain regions must coordinate their activity through dynamic functional interactions, rapidly reconfiguring their activity and connectivity patterns in response to changing cognitive demands and stimulus characteristics." Do they have any specific evidence supporting this claim?

(2) These claims seem overstated: "this work has broad implications for understanding memory function in children, for developing educational interventions that enhance memory formation, and enabling early identification of children at risk for learning disabilities." Can the authors add citations that would support these claims, or if not, remove them?

Author response:

eLife Assessment

This study uses a Bayesian framework to characterize latent brain state dynamics associated with memory encoding and performance in children, as measured with functional magnetic resonance imaging. The novelty of the approach offers valuable insights into memory-related brain activity, but the consideration of developmental changes in memory and brain dynamics, and the evidence to support the proposed mapping between specific states and distinct aspects of memory, are incomplete. This work will be of interest to researchers interested in cognitive neuroscience and the development of memory.

We are grateful to the editor and reviewers for their positive feedback and constructive evaluation. Their comments have identified important areas where the manuscript can be strengthened. Below, we outline our planned revisions.

Reviewer #1 (Public review):

Zeng et al. characterized the dynamic brain states that emerged during episodic encoding and the reactivation of these states during the offline rest period in children aged 8-13. In the study, participants encoded scene images during fMRI and later performed a memory recognition test. The authors adopted the BSDS approach and identified four states during encoding, including an "active-encoding" state. The occupancy rate of, and the state transition rates towards, this active-encoding state positively predicted memory accuracy across participants. The authors then decoded the brain states during pre- and post-encoding rests with the model trained on the encoding data to examine state reactivation. They found that the state temporal profile and transition structure shifted from encoding to post-encoding rest. They also showed that the mean lifetime and stability (measured with self-transition probability) of the "default-mode" state during post-encoding rest predict memory performance. How brain dynamics during encoding and offline rest support long-term memory remains understudied, particularly in children. Thus, this study addresses an important question in the field. The authors implemented an advanced computational framework to identify latent brain states during encoding and carefully characterized their spatiotemporal features. The study also showed evidence for the behavioral relevance of these states, providing valuable insights into the link between state dynamics and successful encoding and consolidation.

We thank Reviewer #1 for the positive feedback on our study. And we would like to thank you for the reviewer's constructive feedback. We plan to incorporate detailed methodological justifications and a thorough limitation analysis. We also plan to enhance the overall logical coherence of the manuscript, ensuring a more robust and scientifically sound presentation.

Weaknesses:

(1) If applicable, please provide information on the decoding performance of states during pre- and post-encoding rests. The Methods noted that the authors applied a threshold of 0.1 z-scored likelihood, and based on Figure S2, it seems like most TRs were assigned a reinstated state during post-encoding rest. It would be useful to know, for the decodable TRs, how strong the evidence was in favor of one state over others. Further, was decoding performance better during post- vs. pre- encoding rest? This is critical for establishing that these states were indeed "reinstated" during rest. The authors showed individual-specific correlations between encoding and post-encoding state distribution, which is an important validation of the method, but this result alone is not sufficient to suggest that the states during encoding were the ones that occurred during rest. The authors found that the state dynamics vary substantially between encoding and rest, and it would be helpful to clarify whether these differences might be related to decoding performance. I am also curious whether, if the authors apply the BSDS approach to independently identify brain states during rest periods (instead of using the trained model from encoding), they find similar states during rest as those that emerged during encoding?

We plan three additional analyses to strengthen the evidence for state reinstatement during rest: First, we will report quantitative decoding confidence metrics for each decoded time point, including the log-likelihood between the winning state and the next-best state. We will compare these distributions between pre- and post-encoding rest to test whether decoding quality differs between conditions, as the reviewer suggests. Second, we will provide a more detailed characterization of the decoding process, including the proportion of TRs that survive the log-likelihood threshold of 0.1 during pre- vs. post-encoding rest and whether this proportion relates to memory performance. Third, we will train an independent BSDS model directly on the rest data (rather than using the encoding-trained model) and assess the degree of correspondence between the independently discovered rest states and the encoding states in terms of amplitude profiles and covariance structures. Convergence between the two approaches would provide strong validation that the encoding-defined states genuinely re-emerge at rest. Together with our evidence from our previous analyses, these additional analyses will strengthen our claims.

(2) During post-encoding rest, the intermediate activation state (S1) became the dominant state. Overall, the paper did not focus too much on this state. For example, when examining the relationship between state transitions and memory performance, the authors also did not include this state as a part of the analyses presented in the paper (lines 203-211). Could the author report more information about this state and/or discuss how this state might be relevant to memory formation and consolidation?

We thank the reviewer for this suggestion. During encoding, S1 had the lowest occupancy (~10%) and showed no significant relationship with memory performance, which led us to interpret it as a non-essential transient configuration. In the revision, we will provide a more thorough characterization of S1, and conduct correlation analyses to probe whether its dynamic properties during post-encoding rest correlate with individual memory performance.

(3) Two outcome measures from the BSDS model were the occupancy rate and the mean lifetime. The authors found a significant association with behavior and occupancy rate in some analyses, and mean lifetime in others. The paper would benefit from a stronger theoretical framing explaining how and why these two different measures provide distinct information about the brain dynamics, which will help clarify the interpretation of results when association with behavior was specific to one measure.

We thank the reviewer for this suggestion. Occupancy rate and mean lifetime, while related, capture fundamentally different aspects of brain state dynamics. Occupancy rate reflects the total proportion of time the brain spends in a given state, capturing the overall prevalence of that configuration across the scanning session. Mean lifetime, by contrast, measures the average uninterrupted duration of each state visit, indexing the temporal stability or persistence of a given network configuration once it is entered. Critically, two states could have identical occupancy rates but very different mean lifetimes, a state visited frequently but briefly versus one visited rarely but sustained, implying distinct underlying neural dynamics. In the context of memory, high occupancy of the active-encoding state may reflect repeated engagement of encoding-optimal circuits, while long mean lifetime of the default-mode state during rest may reflect sustained consolidation-related processing. We will expand the theoretical framework in the revised manuscript to articulate these distinctions and connect them to extant findings suggesting that temporal stability versus frequency of state visits may have dissociable behavioral correlates in working memory and episodic memory (He et al., 2023; Stevner et al., 2019).

(4) For performance on a memory recognition test, d' is a more common metric in the literature as it isolates the memory signal for the old items from response bias. According to Methods (line 451), the authors have computed a different metric as their primary behavioral measure (hits + correction rejections - misses - false alarms). Please provide a rationale for choosing this measure instead. Have the authors considered computing d' as well and examining brain-behavior relationships using d'?

Our primary memory recognition metric computed as (hits + correct rejections − misses − false alarms) / total trials, provides an unbiased linear estimate of discrimination ability that is mathematically consistent with d' in directional effects. We selected this measure because it is particularly robust with limited trial counts per condition (Verde et al., 2006; Wickens, 2001). Nonetheless, we agree that reporting d' is important for comparability with the broader literature. In the revision, we will compute d' for each participant and conduct parallel brain–behavior correlation analyses to demonstrate that our findings are robust across both metrics.

(5) While this study examined brain state dynamics in children, there was no adult sample to compare with. Therefore, it is hard to conclude whether the findings are specific to children (or developing brains). It would be helpful to discuss this point in the paper.

We thank the reviewer for raising this point. While several studies have documented memory-related replay and reinstatement in adults at both the regional and systems levels(Tambini et al., 2017; Wimmer et al., 2020), few have examined whether analogous state-level reinstatement occurs in children. Our study was motivated by this gap: we sought to test whether children show dynamic brain state reinstatement mechanisms similar to those described in adults. However, we acknowledge that without a direct adult comparison, we cannot determine whether the observed patterns are unique to children or reflect general principles of episodic memory organization. In the revised manuscript, we will: (a) frame the study more carefully as examining whether established state-level consolidation mechanisms also operate during childhood, (b) discuss findings in relation to adult studies, and (c) include exploratory analyses of age-related variability in both memory performance and BSDS dynamics within our sample, while acknowledging that the narrow age range (8–13) and small sample size limit the power of such developmental analyses. We will clearly identify the absence of an adult comparison as a limitation.

Reviewer #2 (Public review):

This paper investigates the latent dynamic brain states that emerge during memory encoding and predict later memory performance in children (N = 24, ages: 8 -13 years). A novel computational approach (Bayesian Switching Dynamic Systems, BSDS) discovers latent brain states from fMRI data in an unsupervised and parameter-free manner that is agnostic to external stimuli, resulting in 4 states: an active-encoding state, a default-mode state, an inactive state, and an intermediate state. The key finding is that the percentage of time occupied in the active-encoding state (characterized by greater activity in hippocampal, visual, and frontoparietal regions), as well as greater transitions to this state, predicts memory accuracy. Memory accuracy was also predicted by the mean lifetime and transitions to the default-mode state (characterized by greater activity in medial prefrontal cortex and posterior cingulate cortex) during post-encoding rest. Together, the results provide insights into dynamic interactions between brain regions that may be optimal for encoding novel information and consolidating memories for long-term retention.

We thank Reviewer #2 for recognizing the novelty and broader utility of our methodology and for noting that the manuscript is well-written and concise.

Weaknesses:

(1) The study focuses on middle childhood, but there is a lack of engagement in the Introduction or Discussion about what is known about memory development and the brain during this period. Many of the brain regions examined in this study, particularly frontoparietal regions, undergo developmental changes that could influence their involvement in memory encoding and consolidation. The paper would be strengthened by more directly linking the findings to what is already known about episodic memory development and the brain.

We thank the reviewer for this suggestion. In response, we will substantially expand the Introduction and Discussion to situate our findings within the developmental cognitive neuroscience literature on episodic memory. In particular, we will address the protracted developmental trajectory of frontoparietal regions, the well-documented maturation of hippocampal–cortical connectivity during middle childhood, and how these developmental changes may influence the brain state configurations we observed (He et al., 2023; Ryali et al., 2016). This will provide the necessary developmental context for interpreting our state dynamics results.

(2) A more thorough overview of the BSDS algorithm is needed, since this is likely a novel method for most readers. Although many of the nitty-gritty details can be referenced in prior work, it was unclear from the main text if the BSDS algorithm discovered latent states based on activation patterns, functional connectivity, or both. Figure 1F is not very informative (and is missing labels).

We thank the reviewer for this suggestion. We agree that a more accessible overview of the BSDS algorithm (Lee et al., 2025; Taghia et al., 2018) is needed. In the revision, we will expand the Methods and provide a concise algorithmic overview in the main text that clarifies the following key points: (a) BSDS operates on multivariate time series from the ROIs and infers latent brain states defined jointly by their mean activation patterns (amplitude vectors) and inter-regional covariance matrices (functional connectivity); (b) it employs a hidden Markov model framework with Bayesian inference and automatic relevance determination to identify the number of states without manual specification; and (c) state assignments are made at each TR, yielding a temporal sequence that enables computation of occupancy rates, mean lifetimes, and transition probabilities. We will also revise Figure 1F to include appropriate labels and a clearer schematic of the model's inputs, latent structure, and outputs.

(3) A further confusion about the BSDS algorithm was whether it necessarily had to work on the rest data. Figure 4A suggests that each TR was assigned one of the four states based on the maximum win from the log-likelihood estimation. Without more details about how this algorithm was applied to the rest data, it is difficult to evaluate the claim on page 14 about the spontaneous emergence of the states at rest.

The key methodological point is that the BSDS model, once trained on encoding data, can be applied to new (rest) time series via log-likelihood estimation: for each TR during rest, the model computes the log-likelihood of each state given the observed multivariate signal, and the state with the maximum log-likelihood is assigned to that TR. This "decoding" approach tests whether the spatial configurations learned during encoding are present during rest, rather than fitting new states de novo. We applied a threshold to the log-likelihood values to exclude TRs where the evidence for any single state was weak, thus controlling for potential misassignment. We will substantially clarify this process in the revised Methods and main text, and as described in our response to Reviewer #1 point 1, we will also conduct additional analyses to address the concerns raised.

(4) Although the BSDS algorithm was validated in prior simulations and task-based fMRI using sustained block designs in adults, it is unclear whether it is appropriate for the kind of event-related design used in the current study. Figure 1G shows very rapid state changes, which is quantified in the low mean lifetime of the states (between 1-3 TRs on average) in Figure 4C. On the one hand, it is a strength of the algorithm that it is not necessarily tied to external stimuli. On the other hand, it would be helpful to see simulations validating that rapid transitions between states in fMRI data are meaningful and not due to noise.

This is an important methodological question. The rapid state changes observed in our event-related design (mean lifetimes of 1–3 TRs) differ from the longer state durations typically observed with block designs(He et al., 2023; Zeng et al., 2024), where sustained cognitive demands stabilize brain configurations. We believe these rapid transitions are consistent with the inherent dynamics of event-related encoding, where each trial involves rapid shifts between sensory processing, memory binding, and attentional engagement. Several considerations support the meaningfulness of these transitions: (a) the identified states have interpretable amplitude profiles consistent with well-established memory-related brain systems; (b) state dynamics show statistically significant, directionally consistent correlations with subsequent memory performance; and (c) the transition structure during encoding is distinct from that observed during rest, indicating sensitivity to task demands. Nonetheless, we acknowledge the concern about noise and will conduct additional analyses in the revision to address the concerns raised.

(5) The Methods section mentions that participants actively imagined themselves within the encoded scenes and were instructed to memorize the images for a later test during the post-encoding rest scan. This detail needs to be included in the main text and incorporated into the interpretation of the findings, as there are likely mechanistic differences between spontaneous memory replay/reinstatement vs. active rehearsal.

We thank the reviewer for this suggestion. We will include these experimental details in the main text and incorporate it into the interpretation of our findings in the context of spontaneous memory replay/reinstatement vs. active rehearsal (Liu et al., 2019; Wimmer et al., 2020).

(6) Information about the general linear model used to discover the 16 ROIs that showed a subsequent memory effect are missing, such as: covariates in the model (motion, etc.), group analysis approach (parametric or nonparametric), whether and how multiple-comparisons correction was performed, if clusters were overlapping at all or distinct, if the total number of clusters was 16 or if this was only a subset of regions that showed the effect.

We apologize for the missing methodological details. In the revised manuscript, we will provide complete information on the general linear model used to identify the 16 ROIs, including: the event regressors and parametric modulators included in the model, nuisance covariates (motion parameters, white matter and CSF regressors), the group-level analysis approach and statistical thresholding, the method for multiple-comparisons correction, whether the 16 ROIs represent all significant clusters or a subset, and whether any clusters were spatially overlapping. We will also clarify how peak voxels were selected for ROI definition.

Reviewer #3 (Public review):

This paper uses a novel method to look at how stable brain states and the transitions between them promote memory formation during encoding and post-encoding rest in children. I think the paper has some weaknesses (detailed below) that mean that the authors fall short of achieving their aims. Although the paper has an interesting methodological approach, the authors need better logic, and are potentially "double dipping" in their results - meaning their logic is circular. I think the method that they are using could be useful to the broader neuroimaging community, although they need to make this argument clearer in the paper.

We thank Reviewer #3 for recognizing the novelty of our approach and its potential utility for the broader neuroimaging community.

(1) The authors use children as their study subjects but fail to reconcile why children are used, if the same phenomena are expected to be seen in adults (or only children), and if and how their findings change with age across an age range that ranges from middle childhood into early adolescence. They need to include more consideration for the development of their subject population. The authors should make it clear why and how memory was tested in children and not adults. Are adults and children expected to encode and consolidate in a similar manner to children? Do the findings here also apply to adults? How was the age range of 8-13-year-old children selected? Why didn't the authors look at change with age? Does memory performance change with age? Do the BSDS dynamics change with age in the authors' sample?

Our study was motivated by the observation that while adult studies have documented memory replay and reinstatement, very little is known about whether these dynamic state-level mechanisms operate during middle childhood, a period characterized by substantial improvements in episodic memory ability and ongoing maturation of frontoparietal and hippocampal–cortical circuits. The age range of 8–13 was defined a priori based on typical developmental classifications of middle childhood through early adolescence, representing a period when episodic memory abilities are developing rapidly.

In response to the reviewer's specific questions: (a) we will conduct exploratory analyses testing whether memory accuracy, BSDS state dynamics (occupancy, mean lifetime, transitions), and brain–behavior correlations vary as a function of age within our sample; (b) we will clearly discuss whether adults are expected to show similar patterns, drawing on the extant adult literature; and (c) we will acknowledge as a limitation that our sample size (N = 24) and narrow age range provide limited statistical power for detecting continuous age-related changes, and that a dedicated cross-sectional or longitudinal developmental design would be needed to draw firm conclusions about developmental trajectories. Please also see responses to Reviewer #1 point 5 and Reviewer #2 point 1.

(2) The authors look for brain state dynamics within a preselected set of ROIs that are selected because they display a subsequent memory effect. This is problematic because the state that is most associated with subsequent memory (S3, or State 3) is also the one that shows most activity in these regions (that have already been a priori selected due to displaying a subsequent memory effect). This logic is circular. It would be helpful if they could look at brain state dynamics in a more ROI agnostic whole brain approach so that we can learn something beyond what a subsequent memory analysis tells us. I think the authors are "double dipping" in that they selected regions for further analysis based on a subsequent memory association (remembered > forgotten contrast) and then found states within those regions showing a subsequent memory effect to further analyze for being associated with subsequent memory. Would it be possible instead to do a whole-brain analysis (something a bit more agnostic to findings) using the BSDS framework, and then, from a whole-brain perspective, look for particular brain states associated with subsequent memory? As it stands, it looks like S3 (state 3) has greater overall activation in all brain regions associated with subsequent memory, so it makes sense that this brain state is also most associated with subsequent memory. The BSDS analysis is therefore not adding anything new beyond what the authors find with the simple subsequent memory contrast that they show in Figure 1C. This particularly effects the following findings: (a) active-encoding state occupancy rate correlated positively with memory accuracy, (b) transitions to the active-encoding state were beneficial / Conversely, transitions toward the inactive state (S4) were detrimental, with incoming transitions showing negative correlations with memory accuracy / The active-encoding state serves as a "hub" configuration that facilitates memory formation, while pathways leading to this state enhance performance and transitions away from it impair encoding.

We appreciate this critique, which raises an important concern about analytical circularity.

a) Why BSDS adds information beyond the static subsequent memory contrast. The reviewer notes that S3 (the active-encoding state) shows high activation in the same regions selected by the subsequent memory contrast, and therefore questions whether BSDS provides new information. We respectfully argue that BSDS captures dimensions of neural organization that a static contrast cannot. Specifically: (a) the subsequent memory contrast identifies which regions are differentially active for remembered vs. forgotten items, averaged across the entire encoding session, it provides no temporal information about when or for how long these regions are co-active; (b) BSDS reveals the moment-to-moment temporal evolution of brain states, including the duration and stability of each configuration (mean lifetime), which independently predicts behavior; (c) BSDS uniquely captures transition dynamics, the rates and patterns of switching between states, which we show are predictive of memory in ways not derivable from the contrast map (e.g., transitions from S2→S3 positively predict memory, transitions toward S4 negatively predict memory); and (d) BSDS characterizes the full covariance structure among regions within each state, revealing distinct connectivity patterns (e.g., the high clustering coefficient and global efficiency of S3), which are not captured by univariate activation contrasts. Thus, while the ROI selection is informed by the subsequent memory effect, the information BSDS extracts from those regions, temporal dynamics, transition patterns, and multivariate covariance, is orthogonal to the information used for selection.

b) Additional validation. To directly address the circularity concern empirically, we will conduct additional analysis using ROIs from previous studies (e.g. network templates) / meta-analyses/Neurosynth ROIs (He et al., 2023; Meer et al., 2020; Taghia et al., 2018), without resorting to selection based on the subsequent memory contrast.

(3) The task used to test memory in children seems strange. Why should children remember arbitrary scenes? How this was chosen for encoding needs to be made clear. There needs to be more description of the memory task and why it was chosen. Why was scene encoding chosen? What does scene encoding have to do with the stated goal of (a) "Understanding how children's brains form lasting memories", (b) "optimizing education" and (c) "identifying learning disabilities"? What was the design of the recognition memory test? How many novel scenes were included in the test, and how were they chosen? How close were the "new" images to previously seen "old" images? Was this varied parametrically (i.e., was the similarity between new and old images assessed and quantified?)

Scene encoding was chosen for several reasons: (a) scenes are rich, complex stimuli that engage the hippocampal–parahippocampal memory system, eliciting robust subsequent memory effects suitable for BSDS modeling; (b) scene encoding recruits distributed networks spanning visual cortex, MTL, and frontoparietal regions, enabling detection of multi-region brain states; and (c) scene encoding paradigms have been widely used in both adult and developmental studies of episodic memory and replay(Tambini et al., 2017; Tompary et al., 2017), facilitating comparison with prior work.

Regarding the recognition test: participants viewed 200 images (100 old, 100 new), with novel scenes drawn from the same categories (buildings and natural scenes) but chosen to be perceptually distinct from studied images. Similarity between old and new images was not parametrically manipulated or quantified: we will note this limitation. We will also expand the main text to include full task details and have deleted claims about implications for educational optimization and learning disability identification (see also Reviewer #3 point 7).

(4) They ultimately found four brain states during encoding. It would be helpful if they could make the logic and foundation for arriving at this number clear.

The number of brain states is not predetermined by the user but is automatically determined by the BSDS algorithm through Bayesian automatic relevance determination (ARD). The model is initialized with a maximum number of possible states, and during inference, states that contribute minimally to explaining the data are effectively pruned, their associated parameters are driven to near-zero by the ARD prior. In our data, the model converged on four states. This is a key advantage of BSDS over conventional HMM approaches, which require the user to specify the state number a priori. We will clarify this process in the revised Methods and Results, referencing the original BSDS methodology paper (Taghia et al., 2018) for full mathematical details.

(5) There is already extant work on whether brain states during post-encoding rest predict memory outcomes. This work needs to be cited and referred to. The present manuscript needs to be better situated within prior work. The authors should look at the work by Alexa Tompary and Lila Davachi. They have already addressed many of the questions that the authors seek to answer. The authors should read their papers (and the papers they cite and that cite them) and then situate their work within the prior literature.

We agree that the manuscript must be better situated within the existing literature on post-encoding rest and memory consolidation. We will revise the Introduction and Discussion to further discuss with the foundational work in adults by Tompary & Davachi (2017, Neuron; 2024, eLife) on consolidation-related hippocampal–mPFC representational overlap, as well as Tambini & Davachi (2013, PNAS; 2019, Trends in Cognitive Sciences) on hippocampal persistence during post-encoding rest and awake reactivation(Tambini et al., 2019; Tambini et al., 2017; Tompary et al., 2017). We will explicitly discuss how our BSDS-based approach to state-level reinstatement complements and extends these earlier findings, which largely focused on region-specific pattern similarity or hippocampal–cortical connectivity, by characterizing reinstatement at the level of dynamic, whole-network configurations.

(6) The authors should back up the claim that "successful episodic memory formation critically depends on the temporal coordination between these systems. Brain regions must coordinate their activity through dynamic functional interactions, rapidly reconfiguring their activity and connectivity patterns in response to changing cognitive demands and stimulus characteristics." Do they have any specific evidence supporting this claim?

The claim that episodic memory depends on temporal coordination and dynamic functional interactions is supported by several lines of evidence: (a) within our study, the significant correlations between state transition rates and memory performance directly demonstrate that dynamic inter-state communication predicts memory outcomes; (b) studies showing that hippocampal–prefrontal theta coherence during encoding predicts subsequent memory (e.g., Zielinski et al., 2020)(Zielinski et al., 2020); and (c) recent work demonstrating that rapid reconfiguration of large-scale brain networks supports cognitive functions including working memory (Shine et al., 2018; Braun et al., 2015)(Braun et al., 2015; Shine et al., 2018) and episodic encoding (Phan et al., 2024)(Phan et al., 2024) We will revise this passage to include specific citations and to make clear that our own transition–behavior correlations constitute direct evidence for this claim.

(7) These claims seem overstated: "this work has broad implications for understanding memory function in children, for developing educational interventions that enhance memory formation, and enabling early identification of children at risk for learning disabilities." Can the authors add citations that would support these claims, or if not, remove them?

We thank the reviewer for raising this point. We agree that the current framing overstates the practical implications. We have now removed these claims and remark on future studies that are needed here.

References

(1) Braun, U., Schafer, A., Walter, H., Erk, S., Romanczuk-Seiferth, N., Haddad, L., . . . Bassett, D. S. (2015). Dynamic reconfiguration of frontal brain networks during executive cognition in humans. Proc Natl Acad Sci U S A, 112(37), 11678-11683.

(2) He, Y., Liang, X., Chen, M., Tian, T., Zeng, Y., Liu, J., . . . Qin, S. (2023). Development of brain-state dynamics involved in working memory. Cerebral Cortex.

(3) Lee, B., Young, C. B., Cai, W., Yuan, R., Ryman, S., Kim, J., . . . Menon, V. (2025). Dopaminergic modulation and dosage effects on brain state dynamics and working memory component processes in Parkinson’s disease. Nature Communications, 16(1), 2433.

(4) Liu, Y., Dolan, R. J., Kurth-Nelson, Z., & Behrens, T. E. J. (2019). Human Replay Spontaneously Reorganizes Experience. Cell, 178(3), 640-652.e614.

(5) Meer, J. N. v. d., Breakspear, M., Chang, L. J., Sonkusare, S., & Cocchi, L. (2020). Movie viewing elicits rich and reliable brain state dynamics. Nature Communications, 11(1), 5004.

(6) Phan, A. T., Xie, W., Chapeton, J. I., Inati, S. K., & Zaghloul, K. A. (2024). Dynamic patterns of functional connectivity in the human brain underlie individual memory formation. Nature Communications, 15(1), 8969.

(7) Ryali, S., Supekar, K., Chen, T., Kochalka, J., Cai, W., Nicholas, J., . . . Menon, V. (2016). Temporal Dynamics and Developmental Maturation of Salience, Default and Central-Executive Network Interactions Revealed by Variational Bayes Hidden Markov Modeling. PLoS Comput Biol, 12(12), e1005138.

(8) Shine, J. M., & Poldrack, R. A. (2018). Principles of dynamic network reconfiguration across diverse brain states. Neuroimage, 180, 396-405.

(9) Stevner, A. B. A., Vidaurre, D., Cabral, J., Rapuano, K., Nielsen, S. F. V., Tagliazucchi, E., . . . Kringelbach, M. L. (2019). Discovery of key whole-brain transitions and dynamics during human wakefulness and non-REM sleep. Nature Communications, 10(1), 1035.

(10) Taghia, J., Cai, W., Ryali, S., Kochalka, J., Nicholas, J., Chen, T., & Menon, V. (2018). Uncovering hidden brain state dynamics that regulate performance and decision-making during cognition. Nature Communications, 9(1), 2505.

(11) Tambini, A., & Davachi, L. (2019). Awake Reactivation of Prior Experiences Consolidates Memories and Biases Cognition. Trends in Cognitive Sciences, 23(10), 876-890.

(12) Tambini, A., Rimmele, U., Phelps, E. A., & Davachi, L. (2017). Emotional brain states carry over and enhance future memory formation. Nature Neuroscience, 20(2), 271-278.

(13) Tompary, A., & Davachi, L. (2017). Consolidation Promotes the Emergence of Representational Overlap in the Hippocampus and Medial Prefrontal Cortex. Neuron, 96(1), 228-241.e225.

(14) Verde, M. F., Macmillan, N. A., & Rotello, C. M. (2006). Measures of sensitivity based on a single hit rate and false alarm rate: The accuracy, precision, and robustness of′, A z, and A’. Perception & psychophysics, 68(4), 643-654.

(15) Wickens, T. D. (2001). Elementary signal detection theory: Oxford university press.

(16) Wimmer, G. E., Liu, Y., Vehar, N., Behrens, T. E. J., & Dolan, R. J. (2020). Episodic memory retrieval success is associated with rapid replay of episode content. Nature Neuroscience, 23(8), 1025-1033.

(17) Zeng, Y., Xiong, B., Gao, H., Liu, C., Chen, C., Wu, J., & Qin, S. (2024). Cortisol awakening response prompts dynamic reconfiguration of brain networks in emotional and executive functioning. Proceedings of the National Academy of Sciences, 121(52), e2405850121.

(18) Zielinski, M. C., Tang, W., & Jadhav, S. P. (2020). The role of replay and theta sequences in mediating hippocampal-prefrontal interactions for memory and cognition. Hippocampus, 30(1), 60-72.

eLife Assessment

This important study elucidates the role of the exocyst component EXOC6A at distinct stages of ciliogenesis, which advances our understanding of ciliary membrane remodeling and cilium formation. The authors provide compelling evidence through high quality light and electron microscopic imaging, and careful analysis of knockout cell lines, that EXOC6A interacts with myosin-Va and is dynamically recruited via dynein-, microtubule-, and actin-dependent mechanisms, to support proper formation of the ciliary membrane. The study will be of interest to cell biologists and other researchers interested in vesicular trafficking, organellar membrane dynamics, and ciliogenesis.

Reviewer #2 (Public review):

Summary:

The molecular mechanisms underlying ciliogenesis are not well understood. Previously, work from the same group (Wu et al., 2018) identified myosin-Va as an important protein in transporting preciliary vesicles to the mother vesicles, allowing for initiation of ciliogenesis. The exocyst complex has previously been implicated in ciliogenesis and protein trafficking to cilia. Here, Lin et al. investigate the role of exocyst complex protein EXOC6A in cilia formation. The authors find that EXOC6A localizes to preciliary vesicles, ciliary vesicles, and the ciliary sheath. EXOC6A colocalizes with Myo-Va in the ciliary vesicle and the ciliary sheath, and both proteins are removed from fully assembled cilia. EXOC6A is not required for Myo-Va localization, but Myo-VA and EHD1 are required for EXOC6A to localize in ciliary vesicles. The authors propose that EXOC6A vesicles continually remodel the cilium: FRAP analysis demonstrates that EXOC6A is a dynamic protein, and live imaging shows that EXOC6A fuses with and buds off from the ciliary membrane. Loss of EXOC6A reduces, but does not eliminate, the number of cilia formed in cells. Any cilia that are still present are structurally abnormal, with either bent morphologies or transition zone defects. Overall, the analyses and imaging are well done, and the conclusions are well supported by the data. The work will be of interest to cell biologists, especially those interested in centrosomes and cilia.

Strengths:

The TEM micrographs are of excellent quality. The quality of the imaging overall is very good, especially considering that these are dynamic processes occurring in a small region of the cell. The data analysis is well done and the quantifications are very helpful. The manuscript is well-written and the final figure is especially helpful in understanding the model.

The manuscript has greatly improved after revision. In particular, testing GPR161 and BBS9 localization is helpful evidence to demonstrate that transition zone function is disrupted when EXOC6A is lost. The generation of a second knockout clone and tests of antibody specificity are also great additions.

Weaknesses:

None

Reviewer #3 (Public review):

Summary:

Lin et al report on the dynamic localization of EXOC6A and Myo-Va at pre-ciliary vesicles, ciliary vesicles, and ciliary sheath membrane during ciliogenesis using three-dimensional structured illumination microscopy and ultrastructure expansion microscopy. The authors further confirm the interaction of EXOC6A and Myo-Va by co-immunoprecipitation experiments and demonstrated the requirement of EHD1 for the EXOC6A-labeled ciliary vesicles formation. Additional experiments using gene-silencing by siRNA and pharmacological tools identified the involvement of dynein-, microtubule-, and actin in the transport mechanism of EXOC6A-labeled vesicles to the centriole, as they have previously reported for Myo-Va. Notably, loss of EXOC6A severely disrupts ciliogenesis, with the majority of cells becoming arrested at the ciliary vesicle (CV) stage, highlighting the involvement of EXOC6A at later stages of ciliogenesis. As the authors observe dynamic EXOC6A-positive vesicle release and fusion with the ciliary sheath, this suggests a role in membrane and potentially membrane protein delivery to the growing cilium past the ciliary vesicle stage. While CEP290 localization at the forming cilium appears normal the recruitment of other transition zone components, exemplified by several MKS and NPHP module components, was also impaired in EXOC6A-deficient cells.

Strengths:

- By applying different microscopy approaches, the study provides deeper insight into the spatial and temporal localization of EXOC6A and Myo-Va during ciliogenesis.

- The combination of complementary siRNA and pharmacological tools targeting different components strengthens the conclusions.

- This study reveals a new function of EXOC6A in delivering membrane and membrane proteins during ciliogenesis, both to the ciliary vesicle as well as to the ciliary sheath.

- The overall data quality is high. The investigation of EXOC6A at different time points during ciliogenesis is well schematized and explained.

- The authors confirmed central antibody reagents used in this study and validated key experiments by using two independent knockout clones (for which sequencing information was provided).

Weaknesses:

- The precise molecular function of EXOC6A remains open, as the presented data suggests no involvement of other exocyst components.

Taken together, the authors achieved their goal to elucidate the role of EXOC6A in ciliogenesis, demonstrating its involvement in vesicle trafficking and membrane remodeling in both early and late stages of ciliogenesis. Their findings are supported by experimental evidence. This work is likely to have an impact on the field by expanding our understanding of the molecular machinery underlying cilia biogenesis, particularly the coordination between exocyst components and cytoskeletal transport systems. The methods and data presented offer valuable tools for dissecting vesicle dynamics and cilium formation, providing a foundation for future research into ciliary dysfunction and related diseases. By connecting vesicle trafficking to structural maturation of an organelle, the study adds important context to the broader description of cellular architecture and organelle biogenesis.

Comments on revisions:

We very much appreciate the extra work you put into improving your manuscript and want to congratulate you on your important discovery. We encourage you to keep up the good work!

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Lin et al. studies the role of EXOC6A in ciliogenesis and its relationship with the interactor myosin-Va using a range of approaches based on the RPE1 cell line model. They establish its spatio-temporal organization at centrioles, the forming ciliary vesicle and ciliary sheath using ExM, various super-resolution techniques, and EM, including correlative light and electron microscopy. They also perform live imaging analyses and functional studies using RNAi and knockout. They establish a role of EXOC6A together with myosin-Va in Golgi-derived, microtubule- and actin-based vesicle trafficking to and from the ciliary vesicle and sheath membranes. Defects in these functions impair robust ciliary shaft and axoneme formation due to defective transition zone assembly.

Strengths:

The study provides very high-quality data that support the conclusions. In particular, the imaging data is compelling. It also integrates all findings in a model that shows how EXOC6A participates in multiple stages of ciliogenesis and how it cooperates with other factors.

Weaknesses:

The precise role of EXOC6A remains somewhat unclear. While it is described as a component of the exocyst, the authors do not address its molecular functions and whether it indeed works as part of the exocyst complex during ciliogenesis.

We sincerely thank Reviewer 1 for the thoughtful evaluation of our manuscript and the constructive comments provided. We are especially grateful for the recognition of the quality and significance of our imaging data and the comprehensive model we propose regarding EXOC6A’s role in ciliogenesis. We did not address the function of other components of the exocyst complex during ciliogenesis. However, in our biochemical analyses, Myosin‑Va specifically co‑immunoprecipitated with EXOC6A but not with other exocyst subunits tested (EXOC5 and EXOC7) (Fig. 4E) indicating a selective interaction between EXOC6A and the Myo‑Va transport machinery.

Reviewer #2 (Public review):

Summary:

The molecular mechanisms underlying ciliogenesis are not well understood. Previously, work from the same group (Wu et al., 2018) identified myosin-Va as an important protein in transporting preciliary vesicles to the mother vesicles, allowing for initiation of ciliogenesis. The exocyst complex has previously been implicated in ciliogenesis and protein trafficking to cilia. Here, Lin et al. investigate the role of exocyst complex protein EXOC6A in cilia formation. The authors find that EXOC6A localizes to preciliary vesicles, ciliary vesicles, and the ciliary sheath. EXOC6A colocalizes with Myo-Va in the ciliary vesicle and the ciliary sheath, and both proteins are removed from fully assembled cilia. EXOC6A is not required for Myo-Va localization, but Myo-VA and EHD1 are required for EXOC6A to localize in ciliary vesicles. The authors propose that EXOC6A vesicles continually remodel the cilium: FRAP analysis demonstrates that EXOC6A is a dynamic protein, and live imaging shows that EXOC6A fuses with and buds off from the ciliary membrane. Loss of EXOC6A reduces, but does not eliminate, the number of cilia formed in cells. Any cilia that are still present are structurally abnormal, with either bent morphologies or the absence of some transition zone proteins. Overall, the analyses and imaging are well done, and the conclusions are well supported by the data. The work will be of interest to cell biologists, especially those interested in centrosomes and cilia.

Strengths:

The TEM micrographs are of excellent quality. The quality of the imaging overall is very good, especially considering that these are dynamic processes occurring in a small region of the cell. The data analysis is well done and the quantifications are very helpful. The manuscript is well-written and the final figure is especially helpful in understanding the model.

Weaknesses:

Additional information about the functional and mechanistic roles of EXOC6A would improve the manuscript greatly.

We sincerely thank Reviewer 2 for the thoughtful and encouraging evaluation of our work. We are grateful for the recognition of the strengths of our study, including the quality of the TEM micrographs, the rigor of our imaging and data analysis, and the clarity of our manuscript and proposed model.

We have expanded our analyses in the revised manuscript to better define EXOC6A’s contribution to ciliary function. Specifically, we examined the trafficking of two critical ciliary membrane-associated proteins: GPR161, a G-protein-coupled receptor involved in Sonic hedgehog (Shh) signaling, and BBS9, a core component of the BBSome complex essential for ciliary membrane protein transport. Our new data (Fig. 7C) show that both GPR161 and BBS9 fail to localize to the cilium in EXOC6A knockout cells, in contrast to wild-type controls where their ciliary localization is robust. This new evidence significantly strengthens the understanding of EXOC6A’s role.

Reviewer #3 (Public review):

Summary:

Lin et al report on the dynamic localization of EXOC6A and Myo-Va at pre-ciliary vesicles, ciliary vesicles, and ciliary sheath membrane during ciliogenesis using three-dimensional structured illumination microscopy and ultrastructure expansion microscopy. The authors further confirm the interaction of EXOC6A and Myo-Va by co-immunoprecipitation experiments and demonstrated the requirement of EHD1 for the EXOC6A-labeled ciliary vesicles formation. Additional experiments using gene-silencing by siRNA and pharmacological tools identified the involvement of dynein-, microtubule-, and actin in the transport mechanism of EXOC6A-labeled vesicles to the centriole, as they have previously reported for Myo-Va. Notably, loss of EXOC6A severely disrupts ciliogenesis, with the majority of cells becoming arrested at the ciliary vesicle (CV) stage, highlighting the involvement of EXOC6A at later stages of ciliogenesis. As the authors observe dynamic EXOC6A-positive vesicle release and fusion with the ciliary sheath, this suggests a role in membrane and potentially membrane protein delivery to the growing cilium past the ciliary vesicle stage. While CEP290 localization at the forming cilium appears normal, the recruitment of other transition zone components, exemplified by several MKS and NPHP module components, was also impaired in EXOC6A-deficient cells.

Strengths:

(1) By applying different microscopy approaches, the study provides deeper insight into the spatial and temporal localization of EXOC6A and Myo-Va during ciliogenesis.

(2) The combination of complementary siRNA and pharmacological tools targeting different components strengthens the conclusions.

(3) This study reveals a new function of EXOC6A in delivering membrane and membrane proteins during ciliogenesis, both to the ciliary vesicle as well as to the ciliary sheath.

(4) The overall data quality is high. The investigation of EXOC6A at different time points during ciliogenesis is well schematized and explained.

Weaknesses:

(1) Since many conclusions are based on EXOC6A immunostaining, it would strengthen the study to validate antibody specificity by demonstrating the absence of staining in EXOC6A-deficient cells.

(2) While the authors generated an EXOC6A-deficient cell line, off-target effects can be clone-specific. Validating key experiments in a second independent knockout clone or rescuing the phenotype of the existing clone by re-expressing EXOC6A would ensure that the observed phenotypes are due to EXOC6A loss rather than unintended off-target effects.

(3) Some experimental details are lacking from the materials and methods section. No information on how the co-immunoprecipitation experiments have been performed can be found. The concentrations of pharmacological agents should be provided to allow proper interpretation of the results, as higher or lower doses can produce nonspecific effects. For example, the concentrations of ciliobrevin and nocodazole used to treat RPE1 cells are not specified and should be included. More precise settings for the FRAP experiments would help others reproduce the presented data. Some details for the siRNA-based knockdowns, such as incubation times, can only be found in the figure legends.

Taken together, the authors achieved their goal of elucidating the role of EXOC6A in ciliogenesis, demonstrating its involvement in vesicle trafficking and membrane remodeling in both early and late stages of ciliogenesis. Their findings are supported by experimental evidence. This work is likely to have an impact on the field by expanding our understanding of the molecular machinery underlying cilia biogenesis, particularly the coordination between the exocyst complex and cytoskeletal transport systems. The methods and data presented offer valuable tools for dissecting vesicle dynamics and cilium formation, providing a foundation for future research into ciliary dysfunction and related diseases. By connecting vesicle trafficking to structural maturation of an organelle, the study adds important context to the broader description of cellular architecture and organelle biogenesis.

We sincerely thank Reviewer 3 for the thorough and thoughtful assessment of our manuscript. We greatly appreciate the recognition of the strengths of our study, including the use of advanced microscopy techniques, complementary functional tools, and the conceptual contributions regarding EXOC6A's role in vesicle trafficking and membrane remodeling during ciliogenesis.

Below, we detail how we have addressed the specific suggestions for improvement:

(1) Validation of EXOC6A Immunostaining Specificity

To directly address the reviewer’s concern regarding antibody specificity, we have included new control immunofluorescence panels in Figure S3E-F, which show a complete loss of EXOC6A signal in two independent knockout (KO) clones. These data confirm the specificity of the EXOC6A antibody used throughout the study and reinforce the accuracy of our localization analyses at different stages of ciliogenesis.

(2) Addressing Potential Clone-Specific or Off-Target Effects

To ensure that the observed phenotypes are attributable to EXOC6A loss and not due to off-target effects, we performed parallel analyses using two independent KO clones, all of which exhibited identical defects in ciliogenesis, including arrest at the ciliary vesicle stage and impaired cilia assembly (Fig. S3C-D).

In addition, we conducted rescue experiments by re-expressing EXOC6A in the KO background, which effectively restored ciliogenesis. Quantitative analysis of the rescue data has been added to the revised manuscript (Figure S6B), providing further support that the observed phenotype is specifically due to EXOC6A deficiency.

(3) Expanded Methodological Details

- A detailed protocol for co-immunoprecipitation experiments, including lysis conditions, antibody concentrations, and washing steps.

- The precise concentrations and treatment durations for all pharmacological agents used, including ciliobrevin and nocodazole.

- Comprehensive details on the siRNA-mediated knockdowns, including oligonucleotide sequences, transfection reagents, and incubation durations.

Recommendations for the authors:

Reviewing Editor Comments:

After further consultation, all 3 reviewers agreed that this is an important study with highquality data, in particular the imaging data. They also considered most of the evidence convincing, but overall they termed it "solid" for two main reasons: first, they would have liked to see a validation of the EXOC6A antibody specificity, and second, they suggest that you demonstrate for at least key experiments the phenotypes with a second KO clone, to exclude clonal effects. In principle, rescue would be suited to address this, but the issue here is that the presented rescue is not very robust.

We sincerely thank the Editor and all reviewers for their constructive and thoughtful evaluation of our manuscript. We are especially grateful for the recognition of the highquality imaging data, the experimental rigor, and the significance of our findings to the field of ciliogenesis.

We fully acknowledge the two principal concerns raised during further consultation: (1) the need for validation of EXOC6A antibody specificity, and (2) the importance of confirming the phenotypes in an independent knockout clone to exclude clonal artifacts. We have taken both of these points seriously and have now addressed them through additional experiments and analyses, as detailed below:

(1) Validation Using Independent Knockout Clones

To rigorously validate antibody specificity and eliminate the possibility of clonal variation, we have characterized a second independent EXOC6A knockout (KO) clone. We confirmed complete loss of EXOC6A expression in both clones using three orthogonal approaches: genotyping, immunoblotting, and immunofluorescence (Fig. S3). Both KO clones exhibit indistinguishable phenotypes, including arrest at the ciliary vesicle stage and impaired cilia formation (Fig. S3D). 

(2) Rescue Phenotype Validation with Statistical Significance

In response to concerns about the robustness of the rescue, we have now included statistical analysis of the rescue experiments. A two-tailed Student’s t-test comparing ciliogenesis between the EXOC6A KO and rescue (GFP-EXOC6A re-expression) conditions shows a statistically significant improvement (p = 0.0041) (Fig. S6B). While we acknowledge that the rescue is partial—likely due to limitations of overexpression systems—the statistically significant recovery provides strong genetic evidence that the phenotypes are specific and reversible. These data are now included in the revised Figure S6.

(3) Functional Consequences of EXOC6A Loss on Ciliary Membrane Protein Trafficking

To further strengthen the mechanistic conclusions, we expanded our study to include the trafficking of two functional ciliary membrane proteins. We show that in EXOC6A KO cells, both BBS9 (a component of the BBSome complex) and GPR161 (a GPCR involved in Shh signaling) fail to enter the cilium. These results suggest that EXOC6A is required not only for early structural events in ciliogenesis, but also for establishing a competent transition zone, critical for ciliary membrane protein recruitment. These findings are detailed in the revised Figure 7C and corresponding Results.

We believe that these additional experiments and clarifications directly address the concerns and significantly strengthen the robustness and impact of our study.

The reviewers also made additional suggestions regarding functional and mechanistic insights that would strengthen the manuscript even further.

Reviewer #1 (Recommendations for the authors):

(1) The authors should include control IF panels for the specificity of the EXOC6A stainings at the various ciliogenesis stages using the KO cell line.

We thank the reviewer for this important suggestion. We have now included the requested immunofluorescence (IF) control panels to validate the specificity of the EXOC6A antibody. As shown in the newly added Figure S3, EXOC6A immunofluorescence signal is completely absent in EXOC6A knockout (KO) cells at CV (Fig. S3E) and cilia membrane (Fig. S3F) stages, whereas robust and stage-specific signals are observed in wild-type cells. These results confirm the specificity of the endogenous EXOC6A staining used throughout the study and validate the spatiotemporal localization patterns reported in the main figures.

(2) It would be informative to compare EXOC6A KO and RNAi to determine whether the only partially impaired ciliogenesis phenotype may be a consequence of cellular adaptation.

We appreciate the reviewer’s concern regarding potential cellular adaptation or clonespecific effects. To address this, we examined the ciliogenesis phenotype in two independent EXOC6A KO clones generated using distinct sgRNA targeting strategies. As shown in Figure S3, two independent KO clones displayed a highly consistent phenotype characterized by a pronounced arrest at the ciliary vesicle (CV) stage and a significant reduction in mature cilium formation.

The reproducibility of this phenotype across multiple independently derived clones strongly argues against clonal variability or long-term adaptive compensation as the underlying cause. Instead, these results support the conclusion that the observed ciliogenesis defects are a direct and specific consequence of EXOC6A loss.

(3) It remains unclear whether EXOC6A's function in ciliogenesis is part of the exocyst complex. This is currently implied by the context in which it is introduced and discussed, although the authors avoid any direct statement about this. Do the authors observe similar phenotypes by knocking down any other exocyst subunit? In any case, this issue should be discussed.

We thank the reviewer for raising this conceptual point. This study did not explore the functions of other components of the exocytosis complex during ciliogenesis, which warrants further investigation in the future. However, in our biochemical analyses, Myosin ‑Va specifically co‑immunoprecipitated with EXOC6A but not with other exocyst subunits tested (EXOC5 and EXOC7) (Fig. 4E) indicating a selective interaction between EXOC6A and the Myo‑Va transport machinery.

Reviewer #2 (Recommendations for the authors):

To clarify the roles of EXOC6A in ciliogenesis, I suggest the following:

(1) Myo-Va is involved in both the intracellular and extracellular ciliogenesis pathways. The authors show that EXOC6A has a role in the intracellular ciliogenesis pathway. Does it also participate in the extracellular pathway?

We thank the reviewer for this insightful question. Given that Myo-Va functions in both intracellular and extracellular ciliogenesis pathways, it is indeed plausible that EXOC6A may also participate in the extracellular pathway. However, the current study was specifically focused on elucidating the molecular mechanisms of intracellular ciliogenesis using RPE1 cells, which exclusively undergo this pathway. Assessing EXOC6A’s role in the extracellular pathway would require the use of specialized models (e.g., polarized epithelial cells such as MDCK or IMCD3), which fall beyond the scope of this manuscript.

(2) In the live imaging movies (Fig 3C, 3D, supp movie 4 and 5), the authors observe tubular structures and puncta with EXOC6A and conclude that these are dynamic vesicles/membranes. While the movies are suggestive of membrane-like behavior, it would be helpful to show that these puncta and tubules have membrane, perhaps by astaining with a membrane dye.

We appreciate the reviewer’s suggestion to validate the membrane identity of EXOC6Apositive structures. While we did not perform membrane dye staining in the current study, we agree this approach would provide additional confirmation. Nevertheless, the dynamic behaviors observed in our live-cell imaging—including membrane-like tubulation, fusion, and fission—strongly support the interpretation that EXOC6A puncta and tubules

(3) It is unclear how the EXOC6A tubules and vesicles are delivered, and the extent to which MyoVa plays a role. The authors co-label EXOC6A and MyoVa in Supp Fig 2, but EXOC6A dynamics seem very different here, as compared to Fig 3D - there are fewer tubules and puncta and less movement of either tubules or puncta between time points. Does expression of MyoVa decrease EXOC6A membrane dynamics? Or is it required for EXOC6A membrane dynamics?

We thank the reviewer for this observation. The apparent differences in EXOC6A dynamics between Supplementary Figure 2 and Figure 3D most likely reflect cell-to-cell variability in dynamic behavior, which is common in live-cell imaging. Both figures were derived from the same stable cell line co-expressing EXOC6A and Myo-Va-GTD. Moreover, our analysis shows that Myo-Va-GTD overexpression does not suppress EXOC6A dynamics, nor is it required for membrane remodeling per se. However, Myo-Va is essential for EXOC6A recruitment to the ciliary vesicle, as shown by the loss of EXOC6A localization in Myo-Va KO cells (Fig. 4A).

(4) The authors show that loss of EXOC6A affects the localization of some transition zone proteins. Does this subsequently lead to defects in transition zone function?

We agree with the reviewer that structural defects in the transition zone (TZ) should be linked to its function. To address this, we examined the localization of two wellcharacterized ciliary membrane-associated proteins: BBS9 and GPR161. Both proteins failed to localize to the cilia in EXOC6A knockout cells, despite proper recruitment in wildtype controls (Fig. 7C). Although we did not examine the exact functions of GPR161 and BBS9, our results suggest that the loss of EXOC6A may impair TZ function, particularly its gating capacity for membrane protein trafficking.

(5) Additional information about how the MKS proteins are regulated by EXOC6A would be helpful to understand the mechanisms by which EXOC6A builds the transition zone. Does EXOC6A directly bind to MKS proteins, or are the MKS proteins delivered by EXOC6A-containing vesicles during ciliogenesis?

We appreciate the reviewers' questions regarding the mechanistic relationship between EXOC6A and MKS module proteins. In this study, we did not explore the mechanism by which EXOC6A constructs the transition zone. This is an interesting topic worthy of further investigation in the future.

Reviewer #3 (Recommendations for the authors):

Recommended modifications:

(1) The co-immunoprecipitation experiments suggest an interaction between EXOC6A and Myo-Va; however, the presence of a faint band in the IgG control raises some uncertainty. To reinforce this conclusion, the authors could demonstrate that the interaction is absent in the EXOC6A knockout cell line.

We thank the reviewer for this careful observation. We acknowledge the presence of a faint Myo‑Va signal in the IgG control lane. Myosin‑Va is a highly abundant cytoskeletal motor protein and can occasionally exhibit low‑level nonspecific binding to agarose beads during immunoprecipitation assays. Importantly, the Myo‑Va signal co‑immunoprecipitated with endogenous EXOC6A is substantially stronger and specifically enriched compared with the IgG control, supporting a specific interaction.

(2) Figure S5: The partial rescue of the EXOC6A phenotype is not entirely convincing. A statistical test to assess the significance of the observed differences may help to strengthen the authors' conclusion.

We appreciate the reviewer’s suggestion to validate the rescue experiment. We have now performed a pairwise two‑tailed Student’s t‑test comparing ciliogenesis efficiency between EXOC6A knockout cells and rescue cells expressing GFP‑EXOC6A. As shown in the revised Figure S6 (original Figure S5), re‑expression of EXOC6A resulted in a statistically significant recovery of ciliogenesis (p = 0.0041). While the rescue is partial—likely due to inherent limitations of plasmid‑based expression systems, including variable transfection efficiency and imperfect restoration of endogenous protein levels—the statistically significant improvement confirms that the ciliogenesis defect is specifically caused by EXOC6A loss. Figure S6 and its legend have been updated accordingly.

(3) A detailed description of the EXOC6A knockout strategy should be included.

The Method section has been expanded to include a comprehensive description of the CRISPR/Cas9 ‑ mediated EXOC6A knockout strategy, including sgRNA sequences, genomic target sites, and validation approaches. Additionally, we now include Figure S3, demonstrating complete loss of EXOC6A protein expression in two independent knockout clones, confirming the efficiency and specificity of the gene‑editing strategy.

(4) The labeling in Figure 6 is confusing; assigning a separate letter to each panel would improve clarity.

Figure 6 has been reorganized for clarity: the original panels have been subdivided and relabeled as 6A/6A’ and 6B/6B’, respectively. The figure legend and all corresponding references in the main text have been updated accordingly.

(5) Lines 109-112: The cell line used is not well described. While experts might understand that Dox is used to induce expression of the transgenes, this should be better explained for non-expert readers.

We have revised the text to clearly explain that doxycycline (Dox) is used to induce transgene expression via a Tet‑On inducible system. This clarification has been added to the main text.

(6) Line 180: replace "labels" with "structures".

We have revised the text as suggested.

(7) Line 189: the EXOC6A recruitment to the membrane structures seems to be occurring on a short timescale that should be specified. In this context, "immediately" appears unscientific.

We have revised the sentence to specify that EXOC6A recruitment occurs within seconds, based on our live‑cell imaging data, providing a more accurate temporal description.

(8) Lines 280-282: We recommend rewording to soften this statement. Actin and microtubule inhibitors affect the entire cytoskeletal network; more specific experiments would be required to assess whether the transport of vesicles is defective.

We have reworded the statement to indicate that the accumulation of these vesicles at the mother centrioles is highly sensitive to disruption of dynein or microtubules, suggesting that efficient transport of these vesicles may depend on the integrity of the microtubule network. However, more experiments are required to confirm this conclusion. 

(9) Lines: 428-433: Similarly, we recommend rewording this statement as it presents the authors' current model, which is in line with the presented data but would require more rigorous investigation.

We have revised this section to describe the mechanism as a working model supported by our data, while acknowledging that further investigation will be required to fully establish the proposed hierarchy and molecular details.

Questions and comments to consider:

(1) 15-30% of cells can form cilia-like structures in the EXOC6A KO cells, although membrane transport should be reduced. It would be interesting to investigate whether these cilia are only formed intracellularly and fail to reach the cell surface.

We thank the reviewer for this insightful question. Using both immunofluorescence and electron microscopy, we observed that a subset of ciliary membranes in EXOC6A KO cells do appear to fuse with the plasma membrane. However, due to the low frequency and heterogeneous morphology of these structures, we were unable to reliably quantify this population. 

(2) In the Western blot shown in Figure 4, EXOC6A appears at multiple molecular weights when detected with the anti-EXOC6A antibody. Providing a possible explanation for this shift would be helpful.

We clarify that the apparent molecular weight shift likely results from gel distortion during electrophoretic separation. Importantly, the specificity of the major EXOC6A band was rigorously validated by its complete absence in EXOC6A knockout lysates, confirming that the detected signal corresponds to EXOC6A.

(3) The Western blot in Figure 5B is not fully convincing; including additional independent blots would be nice.

We thank the reviewer for this suggestion. Figure 5B has been replaced with a blot from an independent experiment, improving clarity and reproducibility.

(4) According to the materials and methods section, siRNA-mediated knockdown of targets was performed using a single siRNA per gene, which could result in off-target effects. It would be advised to use several different siRNAs for a single target to exclude off-target effects, cite references or, in case this has been done.

We appreciate this concern. The siRNAs used in this study were previously validated in our earlier work (Wu et al., Nat Cell Biol 2018), where both specificity and efficiency were rigorously tested. We have now explicitly cited this reference in the Materials and Methods section to justify the selection of these reagents.

(5) The abbreviation CFLEM is uncommon for correlative (fluorescence) light and electron microscopy; the authors should consider using the standard abbreviation CLEM.

We have replaced “CFLEM” with the standard term CLEM (Correlative Light and Electron Microscopy) throughout the manuscript and figure legends.

(6) The term "M-centriole" is uncommon and should at least be introduced. The use of the term "mother centriole" is recommended.

We have replaced “M‑centriole” with the standard term “mother centriole” throughout the manuscript and figures.

eLife Assessment

This fundamental study combines in vitro reconstitution experiments and molecular dynamics simulations to elucidate how membrane lipids are transported from the outer to the inner membrane of mitochondria. The authors provide convincing evidence that a positive membrane curvature is critical for membrane lipid extraction. The work will be of broad interest to cell biologists and biochemists.

Reviewer #1 (Public review):

Lipid transfer proteins (LTPs) play a crucial role in the intramembrane lipid exchange within cells. However, the molecular mechanisms that govern this activity remain largely unclear. Specifically, the way in which LTPs surmount the energy barrier to extract a single lipid molecule from a lipid bilayer is not yet fully understood. This manuscript investigates the influence of membrane properties on the binding of Ups1 to the membrane and the transfer of phosphatidic acid (PA) by the LTP. The findings reveal that Ups1 shows a preference for binding to membranes with positive curvature. Moreover, coarse-grained molecular dynamics simulations indicate that positive curvature decreases the energy barrier associated with PA extraction from the membrane. Additionally, lipid transfer assays conducted with purified proteins and liposomes in vitro demonstrate that the size of the donor membrane significantly impacts lipid transfer efficiency by Ups1-Mdm35 complexes, with smaller liposomes (characterized by high positive curvature) promoting rapid lipid transfer.

This study offers significant new insights into the reaction cycle of phosphatidic acid (PA) transfer by Ups1 in mitochondria. The experiments are technically robust and carefully interpreted by the authors. They provide compelling evidence that a positive membrane curvature and the presence of negatively charged phospholipids govern the transfer of PA by the mitochondrial lipid transfer protein Ups1-Mdm35.

Reviewer #2 (Public review):

Summary:

Lipid transfer between membranes is essential for lipid biosynthesis across different organelle membranes. Ups1-Mdm35 is one of the best-characterized lipid transfer proteins, responsible for transferring phosphatidic acid (PA) between the mitochondrial outer membrane (OM) and inner membrane (IM), a process critical for cardiolipin (CL) synthesis in the IM. Upon dissociation from Mdm35, Ups1 binds to the intermembrane space (IMS) surface of the OM, extracts a PA molecule, re-associates with Mdm35, and moves through the aqueous IMS to deliver PA to the IM. Here, the authors analyzed the early steps of this PA transfer - membrane binding and PA extraction - using a combination of in vitro biochemical assays with lipid liposomes and purified Ups1-Mdm35 to measure liposome binding, lipid transfer between liposomes, and lipid extraction from liposomes. The authors found that membrane curvature, a previously overlooked property of the membrane, significantly affects PA extraction but not PA insertion into liposomes. These findings were further supported by MD simulations.

Strengths:

The experiments are well-designed, and the data are logically interpreted. The present study provides an important basis for understanding the mechanism of lipid transfer between membranes.　

Weaknesses:

The physiological relevance of membrane curvature in lipid extraction and transfer still remains open.

Comments on revisions:

The authors have addressed most of my previous concerns, and the manuscript now looks much stronger.

Reviewer #3 (Public review):

The manuscript by Sadeqi et al. studies the interactions between the mitochondrial protein Ups1 and reconstituted membranes. The authors apply synthetic liposomal vesicles to investigate the role of pH, curvature, and charge on the binding of Ups1 to membranes and its ability to extract PA from them. The manuscript is well written and structured. The authors provide all relevant information and reference the appropriate literature in their introduction. The underlying question of how the energy barrier for lipid extraction from membranes is overcome by Ups1 is interesting, and the data presented by the authors offer a valuable new perspective on this process. It is also certainly a challenging in vitro reconstitution experiment, as the authors aim to disentangle individual membrane properties (e.g., curvature, charge, and packing density) to study protein adsorption and lipid transfer.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Lipid transfer proteins (LTPs) play a crucial role in the intramembrane lipid exchange within cells. However, the molecular mechanisms that govern this activity remain largely unclear. Specifically, the way in which LTPs surmount the energy barrier to extract a single lipid molecule from a lipid bilayer is not yet fully understood. This manuscript investigates the influence of membrane properties on the binding of Ups1 to the membrane and the transfer of phosphatidic acid (PA) by the LTP. The findings reveal that Ups1 shows a preference for binding to membranes with positive curvature. Moreover, coarse-grained molecular dynamics simulations indicate that positive curvature decreases the energy barrier associated with PA extraction from the membrane. Additionally, lipid transfer assays conducted with purified proteins and liposomes in vitro demonstrate that the size of the donor membrane significantly impacts lipid transfer efficiency by Ups1-Mdm35 complexes, with smaller liposomes (characterized by high positive curvature) promoting rapid lipid transfer.

This study offers significant new insights into the reaction cycle of phosphatidic acid (PA) transfer by Ups1 in mitochondria. Notably, the authors present compelling evidence that, alongside negatively charged phospholipids, positive membrane curvature enhances lipid transfer - an effect that is particularly relevant at the mitochondrial outer membrane. The experiments are technically robust, and my primary feedback pertains to the interpretation of specific results.

(1) The authors conclude from the lipid transfer assays (Figure 5) that lipid extraction is the rate-limiting step in the transfer cycle. While this conclusion seems plausible, it should be noted that the authors employed high concentrations of Ups1-Mdm35 along with less negatively charged phospholipids in these reactions. This combination may lead to binding becoming the rate-limiting factor. The authors should take this point into consideration. In this type of assay, it is challenging to clearly distinguish between binding, lipid extraction, and membrane dissociation as separate processes.

We have included a detailed consideration of this issue on page 11 of the revised manuscript.

(2) The authors should discuss that variations in the size of liposomes will also affect the distance between them at a constant concentration, which may affect the rate of lipid transfer. Therefore, the authors should determine the average size and size distribution of liposomes after sonication (by DLS or nanoparticle analyzer, etc.)

We have included DLS measurements for all lipid sizes (page 6) (SupFig. 2A). Due to the sensitivity of the intensity distribution in DLS measurements by larger particles, we also conducted cryo-EM analysis of vesicles with different sizes (page 6) (SupFig. 2B).

We also now discuss the challenges posed by a fixed membrane-binding surface, which can lead to variations in vesicle spacing when using liposomes of different sizes and its possible influence on the interpretation of results (page 10-11).

(3) The authors use NBD-PA in the lipid transfer assays. Does the size of the donor liposomes affect the transfer of NBD-PA and DOPA similarly? Since NBD-labeled lipids are somewhat unstable within lipid bilayers (as shown by spontaneous desorption in Figure 5B), monitoring the transfer of unlabeled PA in at least one setting would strengthen the conclusion of the swap experiments.

To experimentally address this comment, we explored several different approaches. We first performed transfer experiments using unlabelled lipids, following the general procedures described in the manuscript. After the transfer reaction, we attempted to separate donor and acceptor vesicles by centrifugation and subsequently analyzed the samples by high-resolution mass spectrometry and thin-layer chromatography. Despite considerable effort, we were not able to reliably separate the differently sized liposomes. In particular, small liposomes proved difficult to handle during centrifugation, which is a well-known challenge (Kučerka et al. 1994, BBA; Boucrot et al. 2012, Cell). In addition, liposomes exhibited a tendency to cross-link in the presence of protein, further complicating the separation. Even if this separation step were straightforward, an important limitation of such an approach is that it is very difficult to monitor lipid transfer with sufficient time resolution. Much of the relevant activity occurs within the first 20–30 seconds, and precise interruption at defined time points would be essential.

We therefore set out to establish a fluorescence-based assay that would allow us to follow lipid transfer in real time. For this, we adapted a dequenching-type assay based on a PE coupled fluorescein dye, whose fluorescence is quenched in the proximity of negative charges (e.g., negatively charged lipid headgroups). In principle, this assay should allow us to monitor the movement of negatively charged PA lipids away from donor membranes. Although a fluorescein-based passive lipid-transfer assay has been described previously (Richens et al., 2017), it is used only rarely in the lipid-transfer field. While establishing this assay, we encountered several technical challenges. For example, immediately after protein addition, fluorescence intensity changed in unexpected ways that could not be attributed to lipid transfer. Such effects have been reported in the literature (Wall et al., 1995) and are most likely caused by changes in membrane charge density upon protein binding. After extensive fine -tuning of the experimental conditions and careful evaluation of the data, we were ultimately able to demonstrate that lipid-transfer rates are significantly higher with smaller than with larger liposomes. These results confirm our initial observations, and importantly, they were obtained using unlabelled PA.

The revised manuscript now includes this independent lipid-transfer assay demonstrating the transfer of non-labelled PA (page 11) (SupFig. 4).

(4) The present study suggests that membrane domains with positive curvature at the outer membrane may serve as starting points for lipid transport by Ups1-Mdm35. Is anything known about the mechanisms that form such structures? This should be discussed in the text.

We included a detailed consideration of this interesting point in the discussion section on page 13-14.

Reviewer #2 (Public review):

Summary:

Lipid transfer between membranes is essential for lipid biosynthesis across different organelle membranes. Ups1-Mdm35 is one of the best-characterized lipid transfer proteins, responsible for transferring phosphatidic acid (PA) between the mitochondrial outer membrane (OM) and inner membrane (IM), a process critical for cardiolipin (CL) synthesis in the IM. Upon dissociation from Mdm35, Ups1 binds to the intermembrane space (IMS) surface of the OM, extracts a PA molecule, re-associates with Mdm35, and moves through the aqueous IMS to deliver PA to the IM. Here, the authors analyzed the early steps of this PA transfer - membrane binding and PA extraction - using a combination of in vitro biochemical assays with lipid liposomes and purified Ups1-Mdm35 to measure liposome binding, lipid transfer between liposomes, and lipid extraction from liposomes. The authors found that membrane curvature, a previously overlooked property of the membrane, significantly affects PA extraction but not PA insertion into liposomes. These findings were further supported by MD simulations.

Strengths:

The experiments are well-designed, and the data are logically interpreted. The present study provides an important basis for understanding the mechanism of lipid transfer between membranes.

Weaknesses:

The physiological relevance of membrane curvature in lipid extraction and transfer still remains open.

We thank the reviewer for the constructive feedback on our work. We agree that the physiological relevance of membrane curvature in lipid extraction and transfer remains an open question. Our data show that Ups1 binding to native-like OM membranes under physiological pH conditions is curvature-dependent, supporting the idea that this mechanism may optimize lipid transfer in vivo. While the intricate biophysical basis of this behaviour can only be dissected in vitro, these findings offer valuable insight into how curvature may functionally regulate Ups1 activity in the cellular context. To directly test this, it will be important in future studies to identify Ups1 mutants that lack curvature sensitivity and assess their performance in vivo, which will help clarify the physiological importance of this mechanism.

Reviewer #3 (Public review):

The manuscript by Sadeqi et al. studies the interactions between the mitochondrial protein Ups1 and reconstituted membranes. The authors apply synthetic liposomal vesicles to investigate the role of pH, curvature, and charge on the binding of Ups1 to membranes and its ability to extract PA from them. The manuscript is well written and structured. With minor exceptions, the authors provide all relevant information (see minor points below) and reference the appropriate literature in their introduction. The underlying question of how the energy barrier for lipid extraction from membranes is overcome by Ups1 is interesting, and the data presented by the authors could offer a valuable new perspective on this process. It is also certainly a challenging in vitro reconstitution experiment, as the authors aim to disentangle individual membrane properties (e.g., curvature, charge, and packing density) to study protein adsorption and lipid transfer. I have one major suggestion and a few minor ones that the authors might want to consider to improve their manuscript and data interpretation:

Major Comments:

The experiments are performed with reconstituted vesicles, which are incubated with recombinant protein variants and quantitatively assessed in flotation and pelleting assays. According to the Materials and Methods section, the lipid concentration in these assays is kept constant at 5 µM. However, the authors change the size of the vesicles to tune their curvature. Using the same lipid concentration but varying vesicle sizes results in different total vesicle concentrations. Moreover, larger vesicles (produced by freeze-thawing and extrusion) tend to form a higher proportion of multilamellar vesicles, thus also altering the total membrane area available for binding. Could these differences in the experimental system account for the variation in binding? To address this, the authors would need to perform the experiments either under saturated (excess protein) conditions or find an experimental approach to normalize for these differences.

To experimentally address this comment, we have conducted a detailed structural analysis of liposomes of different sizes using cryo-EM to determine the degrees of multi-lamellarity and to estimate how much membrane surface is available for protein binding. We found that while indeed as expected liposomes extruded through a 400 nm sized filter showed about 75 % of the initially calculated membrane surface is still available (SupFig. 3A). For 50 nm extruded liposomes, this number went up to about 93 % and for sonicated liposomes the number was about 94 %. Given the fact that we found about 70 % binding of Ups1 to sonicated liposomes, while this number went down to about 40 % with 50 nm liposomes and to about 30 % for 400 nm extruded liposomes, we can rule out that the effects we observe are due to an increased or decreased available membrane binding area.

Additionally, we performed experiments with increasing amounts of lipids to analyse the impact of lipid concentration on Ups1 membrane binding, when comparing 400 nm extruded liposomes with sonicated liposomes. Interestingly, while we do observe an increased binding of Ups1 to sonicated liposomes with concentrations varying between 2.5 mM to 10 mM no major increase in binding was observed with 400 nm extruded liposomes. Ups1 membrane binding to sonicated liposomes highly exceeded binding to 400 nm extruded liposomes under all tested conditions (page 7) (SupFig. 3B).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors:):

(1) Figures 1, 2, and 3 - In the flotation assays, the Ups1-containing fractions differ between experiments. The presence of liposomes in these fractions should be confirmed, for example, by fluorescence measurements. In relation to this, the broad low MW bands in Supplementary Figure 3 may reflect liposomes (mixed micelles of lipids and SDS?), as their fractionation patterns coincide with those of Ups1 at pH 5.5 -6.7 but deviate at pH 7.0 and 7.5. Could the authors clarify this discrepancy?

Flotation profiles vary with changing conditions of the experiment. We have included a picture of a gel showing the Coomassie staining and the fluorescence of the used lipids side by side to show that the protein bands co-migrate together with liposomes (SupFig. 5). 

(2) Figures 2, 3, and 5 - The sizes of the liposomes (400 nm and 50 nm) should be experimentally confirmed, e.g., by dynamic light scattering (DLS).

We have included DLS measurements confirming the differences of liposome sizes. Please see answer to point 2 of Reviewer 1.

(3) Figure 4C - The free energy landscape for different phospholipids is interesting. What about other acidic phospholipids, such as PS?

This is indeed an interesting point. Our molecular dynamics simulations show that PE has a similar free energy landscape to PA while PC is significantly different. This might point into the direction that the headgroup size plays a major role. For intra-mitochondrial PS transport a specific protein complex consisting of Ups2/Mdm35 has been identified, and it will be an interesting question for future studies if PS transfer is regulated by similar factors.

(4) Supplementary Figure 2 - The deformation of liposomes by Ups1 is interesting. Does this depend on the presence of PA or other acidic phospholipids?

We asked ourself the same question throughout the project. As pointed out in the manuscript, the membrane-deforming activity of Ups1 is relatively mild when compared to proteins found for example in endocytosis. This made a proper static analysis challenging. We weren’t able to unambiguously show whether other acidic phospholipids showed comparable effects to PA.

(5) It may not be easy to assess experimentally, but the OM in mitochondria should have scramblase activity. Then, such scramblase activity could influence the observed effects of membrane curvature on Ups1-mediated PA transfer.

(6) It would be helpful to discuss this possibility in the manuscript.

In the revised version of the manuscript, we now discuss the existence of scramblases, such as Sam50 and VDAC, in the outer mitochondrial membrane with regard to their likely effect on membrane packing (page 13 - 14). As for a co-reconstitution experiment we considered the in vitro analysis of the impact that a scramblase in liposomes might have on lipid transfer outside the scope of this study. 

(7) Figure 6 is not referenced in the main text.

Thank you, this oversight was corrected.

(8) The non-abbreviated forms of LUV and SUV should be defined in the text upon first use.

We now include a definition in the manuscript.

(9) The term "transfer velocity" would be better expressed as "transfer rate".

We agree, and we changed the wording accordingly.

Reviewer #3 (Recommendations for the authors):

(1) As flotation assays are a central technique of the study, readers who are not familiar with this method could benefit from a few explanatory sentences and appropriate references in the introduction section.

Figure 1B now contains an updated version of a cartoon outlining the flotation assay and a description in the manuscript (page 4) that should make it easier to understand the assay. We have also included a direct reference within the methods section to a paper describing this assay in more detail.

(2) Related to the major point, but also to improve the manuscript overall, the authors could add DLS (for size distribution and zeta potential) and cryo-EM (for multilamellarity analysis) data. This would aid future efforts to reproduce their observations.

In the revised version of the manuscript we include DLS and zeta potential measurements as well as a detailed analysis of liposome multilamellarity by cryo-EM (also see answer to point 2 by Reviewer 1) (SupFig. 2A & B; SupFig. 3E).

(3) Could the authors state the specific zeta potentials of the negatively charged (under varying pH) and neutral liposomes and relate these to natural membranes?

We have included zeta potential measurements of differently charged liposomes in and changed the text accordingly (page 8) (SupFig. 3E).

(4) Changes in pH affect several characteristics of membranes (including lipid dipoles, charge, packing density, fluidity, and phase separation), particularly charge density. This experimental system does not allow all of these factors to be disentangled and studied separately. Some of the observations presented in Figures 2 and 5 could also be explained by these effects.

The effects of pH on various membrane properties, such as lipid headgroup dipoles, lipid packing, interfacial tension, and others, are well described in the literature. For example, it was implied that increasing pH leads to phosphatidic acid (PA) becoming more negatively charged when in proximity to phosphatidylethanolamine (PE). We already discuss this effect in the manuscript, as our observation that Ups1 binding to membranes depends on negatively charged lipids but nevertheless increases with decreasing pH is unexpected.

As pointed out, many of the parameters mentioned above are beyond control in our assays, and a systematic analysis of each of these factors with respect to Ups1 membrane binding and lipid transfer would be well beyond the scope of this manuscript. We have therefore included a passage discussing this issue in more detail (page 4-5).

(5) Is the curvature simulated in the theoretical models comparable to the curvature of the liposome systems (e.g., a sphere of 100 nm diameter)?

The simulated curvature spans a defined range, with the highest curvature corresponding to vesicles with diameters of approximately 15 nm. This corresponds reasonably well to the vesicle size distribution as analyzed by cryo-EM.

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