Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, James Lee, Lu Bai, and colleagues use a multifaceted approach to investigate the relationship between transcription factor condensate formation, transcription, and 3D gene clustering of the MET regulon in the model organism S. cerevisiae. This study represents a second clear example of inducible transcriptional condensates in budding yeast, as most evidence for transcriptional condensates arises from studies of mammalian systems. In addition, this study links the genomic location of transcriptional condensates to the potency of transcription of a reporter gene regulated by the master transcription factor contained in the condensate. The strength of evidence supporting these two conclusions is strong. Less strong is evidence supporting the claim that Met4-containing condensates mediate the clustering of genes in the MET regulon.

Strengths:

The manuscript is for the most part clearly written, with the overriding model and specific hypothesis being tested clearly explained. Figure legends are particularly well written. An additional strength of the manuscript is that most of the main conclusions are supported by the data. This includes the propensity of Met4 and Met32 to form puncta-like structures under inducing conditions, formation of Met32-containing LLPS-like droplets in vitro (within which Met4 can colocalize), colocalization of Met4-GFP with Met4-target genes under inducing conditions, enhanced transcription of a Met3pr-GFP reporter when targeted within 1.5 - 5 kb of select Met4 target genes, and most impressively, evidence that several MET genes appear to reposition under transcriptionally inducing conditions. The latter is based on a recently reported novel in vivo methylation assay, MTAC, developed by the Bai lab.

Weaknesses:

My principal concern is that the authors fail to show convincing evidence for a key conclusion, highlighted in the title, that nuclear condensates per se drive MET gene clustering. Figure 4E demonstrates that Met4 molecules, not condensates per se, are necessary for fostering distant cis and trans interactions between MET6 and three other Met4 targets under -met inducing conditions. In addition, the paper would be strengthened by discussing a recent study conducted in yeast that comes to many of the same conclusions reported here, including the role of inducible TF condensates in driving 3D genome reorganization (Chowdhary et al, Mol. Cell 2022).

Following the reviewer’s advice, we carried out MTAC with the VP near MET6 in WT Met4 and ΔIDR2.3 strains (results shown below). The conclusions are somewhat ambiguous. For long-distance interactions with MUP1, YKG9, STR3, and MET13, we indeed observe decreased MTAC signals close to background levels in the ΔIDR2.3 strain, which aligns with the model suggesting that Met4 condensation promotes clustering among Met4 targeted genes. However, we also noticed significant decreases in the local MTAC signals (HIS3 and MET6). It is possible that the changes in Met4 condensates alter the chromosomal folding near MET6, thereby affecting the local MTAC signals. Alternatively, LacI-M.CviPI (the methyltransferase) could be induced to a lesser extent in the ΔIDR2.3 strain, leading to a genome-wide decrease in MTAC signals. Due to this ambiguity, we decided not to include the following plot in the main figure.

Author response image 1.

We discussed Hsf1 and added the suggested reference on page 13.

Other concerns:

(1) A central premise of the study is that the inducible formation of condensates underpins the induction of MET gene transcription and MET gene clustering. Yet, Figure 1 suggests (and the authors acknowledge) that puncta-like Met4-containing structures pre-exist in the nuclei of non-induced cells. Thus, the transcription and gene reorganization observed is due to a relatively modest increase in condensate-like structures. Are we dealing with two different types of Met4 condensates? (For example, different combinations of Met4 with its partners; Mediator- or Pol II-lacking vs. Mediator- or Pol II-containing; etc.?) At the very least, a comment to this effect is necessary.

Although Met4 can form smaller puncta in the +met condition (Figure 1A), it cannot be recruited to its target genes due to the absence of its sequence-specific binding partners, Met31 and Met32 (these two factors are actively degraded in the +met condition). Consistently, in the +met condition, Met4 shows extremely low genome-wide ChIP signals (Figure 3C). Therefore, these Met4 puncta in +met do not have organize the 3D genome or have gene regulatory functions. This discussion is added on page 12.

(2) Using an in vitro assay, the authors demonstrate that Met4 colocalizes with Met32 LLPS droplets (Figure 2F). Is the same true in vivo - that is, is Met32 required for Met4 condensation? This could be readily tested using auxin-induced degradation of Met32. Along similar lines, the claim that Met32 is required for MET gene clustering (line 250) requires auxin-induced degradation of this protein.

As the reviewer pointed out above, cells in the +met condition also show small Met4 puncta. In this condition, Met32 is essentially undetectable (Met31 level is even lower and remains undetectable even in the -met conditions). Therefore, Met4 does not strictly require the presence of Met32 in vivo (may require other factors or modifications). Met4 does not have DNA-binding activity, and therefore it cannot target and organize chromosomes on its own. Although we did not do the Met32 degradation experiment, we measured the 3D genome conformation in +met and showed that there are no detectable interactions among Met4 target genes.

(3) The authors use a single time point during -met induction (2 h) to evaluate TF clustering, transcription (mRNA abundance), and 3D restructuring. It would be informative to perform a kinetic analysis since such an analysis could reveal whether TF clustering precedes transcriptional induction or MET gene repositioning. Do the latter two phenomena occur concurrently or does one precede the other?

We appreciate the reviewer’s insightful question. It is indeed intriguing to consider whether TF clustering precedes transcriptional induction and MET gene clustering. However, as mentioned on page 12 of our manuscript, this experiment poses significant challenges. The low intensities of the Met4 and Met32 signals necessitate high excitation for imaging, which also makes them prone to photo-bleaching. Consequently, we have been unable to measure the dynamics of Met4 and Met32 puncta in vivo, let alone co-image them with DNA/RNA. Undertaking this experiment will require considerable effort, which we plan to pursue in the future.

(4) Based on the MTAC assay, MET13 does not appear to engage in trans interactions with other Met4 targets, whereas MET6 does (Figures 4C and 4E). Does this difference stem from the greater occupancy of Met4 at MET6 vs. MET13, greater association of another Met co-factor with the chromatin of MET6 vs. MET13, or something else?

We were also surprised by this result, given that MET13 emerged as one of the strongest transcriptional hotspots in our previous screen. It also exhibits one of the highest Met4 ChIP signals and is closely associated with the nuclear pore complex. Our earlier findings indicate that DNA dynamics near the VP significantly influence the MTAC signal; specifically, a VP with constrained motion is less effective at methylating interacting sites (Li et al., 2024). Therefore, it is plausible that MET13 is associated with a large Met4 condensate, which constrains the motion of nearby chromatin and diminishes MTAC efficiency.

Reviewer #2 (Public Review):

Summary:

This manuscript combines live yeast cell imaging and other genomic approaches to study how transcription factor (TF) condensates might help organize and enhance the transcription of the target genes in the methionine starvation response pathway. The authors show that the TFs in this response can form phase-separated condensates through their intrinsically disordered regions (IDRs), and mediate the spatial clustering of the related endogenous genes as well as reporter inserted near the endogenous target loci.

Strengths:

This work uses rigorous experimental approaches, such as imaging of endogenously labeled TFs, determining expression and clustering of endogenous target genes, and reporter integration near the endogenous target loci. The importance of TFs is shown by rapid degradation. Single-cell data are combined with genomic sequencing-based assays. Control loci engineered in the same way are usually included. Some of these controls are very helpful in showing the pathway-specific effect of the TF condensates in enhancing transcription.

Weaknesses:

Perhaps the biggest weakness of this work is that the role of IDR and phase separation in mediating the target gene clustering is unclear. This is an important question. TF IDRs may have many functions including mediating phase separation and binding to other transcriptional molecules (not limited to proteins and may even include RNAs). The effect of IDR deletion on reduced Fano number in cells could come from reduced binding with other molecules. This should be tested on phase separation of the purified protein after IDR deletion. Also, the authors have not shown IDR deletion affects the clustering of the target genes, so IDR deletion may affect the binding of other molecules (not the general transcription machinery) that are specifically important for target gene transcription. If the self-association of the IDR is the main driving force of the clustering and target gene transcription enhancement, can one replace this IDR with totally unrelated IDRs that have been shown to mediate phase separation in non-transcription systems and still see the gene clustering and transcription enhancement effects? This work has all the setup to test this hypothesis.

We thank the reviewer for raising this point, and we tried more in vitro and in vivo experiments with Met4 IDR deletions. See the answer to Reviewer 1 for the in vivo 3D mapping experiment.

We purified Met4-ΔIDR2 with an MBP tag, but its low yield made labeling and conducting thorough experiments challenging. At concentrations above ~10 μM, the protein tends to aggregate, while at lower concentrations, it remains diffusive in solution and does not form condensates. When we mixed purified Met4-ΔIDR2 with Met32, we observed reduced partitioning inside Met32 condensates compared to the full-length Met4. As the reviewer noted, this diminished interaction may contribute to the decreased puncta formation observed in vivo. This result is added to the manuscript on page 11 and supplementary figure 5.

The Met4 protein was tagged with MBP but Met 32 was not. MBP tag is well known to enhance protein solubility and prevent phase separation. This made the comparison of their in vitro phase behavior very different and led the authors to think that maybe Met32 is the scaffold in the co-condensates. If MBP was necessary to increase yield and solubility during expression and purification, it should be cleaved (a protease cleavage site should be engineered) to allow phase separation in vitro.

Following the reviewer’s advice, we purified Met4-TEV-MBP so that the MBP can be cleaved off. Unfortunately, concentrated Met4-TEV-MBP needs to be stored at high salt (400mM) to be soluble. When exchanged into a suitable buffer for TEV cleavage (≤200 mM NaCl), nearly all soluble protein aggregates. Attempts to digest the protein in storage buffer results in observable aggregation before significant cleavage (see below).  

Author response image 2.

Are ATG36 and LDS2 also supposed to be induced by -met? This should be explained clearly. The signals are high at -met.

Genomic loci ATG36 and LDS2 were chosen as controls because they are not bound by Met TFs (ChIP-seq tracks) and their expressions are not induced by -met (RNA-seq data). This information is added to the manuscript on page 9. When MET3pr-GFP reporter is inserted into these loci, GFP is induced by -met (because it is driven by the MET3 promoter), but the induction level is less than the same reporter inserted into the transcriptional hotspot like MET13 and MET6 (Figure 6E, also see Du et al., Plos Genetics, 2017).

ChIP-seq data:

Author response image 3.

RNA-seq counts:

Author response table 1.

Figure 6B, the Met4-GFP seems to form condensates at all three loci without a very obvious difference, though 6C shows a difference. 6C is from only one picture each. The authors should probably quantify the signals from a large number of randomly selected pictures (cells) and do statistics.

If we understand this comment correctly, the reviewer is referring to the fact that all three loci in Figure 6B appear to show a peak in GFP intensity. This pattern emerges because these images are averaged among many cells (number of cells analyzed in 6B has been added to the Figure legends). GFP intensities near the center will always be higher because peripheral pixels are more likely to fall outside the nuclei boundaries, where Met4 signals are absent (same as in Figure 3F). Importantly, MET6 locus shows higher intensity near the center in comparison to PUT1 and ATG36, indicating its co-localization with Met4 condensates.

Reviewer #3 (Public Review):

Summary:

In this study, the authors probe the connections between clustering of the Met4/32 transcription factors (TFs), clustering of their regulatory targets, and transcriptional regulation. While there is an increasing number of studies on TF clustering in vitro and in vivo, there is an important need to probe whether clustering plays a functional role in gene expression. Another important question is whether TF clustering leads to the clustering of relevant gene targets in vivo. Here the authors provide several lines of evidence to make a compelling case that Met4/32 and their target genes cluster and that this leads to an increase in transcription of these genes in the induced state. First, they found that, in the induced state, Met4/32 forms co-localized puncta in vivo. This is supported by in vitro studies showing that these TFs can form condensates in vitro with Med32 being the driver of these condensates. They found that two target genes, MET6 and MET13 have a higher probability of being co-localized with Met4 puncta compared with non-target loci. Using a targeted DNA methylation assay, they found that MET13 and MET6 show Met4-dependent long-range interactions with other Met4-regulated loci, consistent with the clustering of at least some target genes under induced conditions. Finally, by inserting a Met4-regulated reporter gene at variable distances from MET6, they provide evidence that insertion near this gene is a modest hotspot for activity.

Weaknesses:

(1) Please provide more information on the assay for puncta formation (Figure 1). It's unclear to me from the description provided how this assay was able to quantitate the number of puncta in cells.

Due to the variation in puncta size and intensity (as illustrated in Figure 1A), counting the number of puncta would be highly subjective with arbitrary cutoffs. Therefore, we chose to calculate the CV and Fano values instead, which are unbiased measures. Proteins that form puncta will exhibit greater pixel-to-pixel variations in GFP intensity, resulting in higher CV and Fano values.

(2) How does the number of puncta in cells correspond with the number of Met-regulated genes? What are the implications of this calculation?

As previously mentioned, defining the exact number of Met4 puncta is challenging. The number of puncta does not necessarily have one-to-one correspondence to the number of Met4 target genes. Some puncta may not be associated with chromosomes, while others may interact with multiple genes.

(3) A control for chromosomal insertion of the Met-regulated reporter was a GAL4 promoter derivative reporter. However, this control promoter seems 5-10 fold more active than the Met-regulated promoter (Figure 6). It's possible that the high activity from the control promoter overcomes some other limiting step such that chromosomal location isn't important. It would be ideal if the authors used a promoter with comparable activity to the Met-reporter as a control.

We agree with the reviewer that it will be better to use another promoter with comparable activity. Indeed, this was our rationale for selecting the attenuated GAL1 promoter over the WT version; however, it still exhibited substantially higher activity than the MET3pr. Unfortunately, we do not have a promoter from a different pathway that is calibrated to match the activity level of MET3pr. Nonetheless, MET17pr has much higher activity (~3 fold) than MET3pr, and we observed similar degree of stimulus from the hotspot in comparison to the control locus for both promoters (1.5-2-fold increase in GFP expression) (Figure 6E & F). This suggests that the observed effects are more likely to depend on the activation pathway and TF identity rather than the promoter strength.

(4) It seems like transcription from a very large number of genes is altered in the Met4 IDR mutant (Figure 7F). Why is this and could this variability affect the conclusions from this experiment?

We agree with the reviewer that ΔIDR 2.3 truncation affects the expression of 2711 (P-adj <0.05) genes (1339 up,1372 down). We suspect that this is due to the decreased expression of Met4 target genes, leading to altered levels of methionine and other sulfur-containing metabolites. Such changes would have a global impact on gene expression. Importantly, despite the similar number of genes that show up vs down regulation in the ΔIDR 2.3 strain, almost all Met4 targets showed decreased expression (Fig 7F). This supports the model where Met4 condensates lead to increased expression in its target genes.

Recommendations for the authors:

Reviewer #1 (Recommendations for The Authors):

(1) The introduction contains multiple miscitations. Rather than gene clustering, most of the studies and reviews cited (e.g., lines 35-39) report interactions between genomic loci (E-E, E-P, and P-P). There are other claims not supported by the papers cited. Moreover, the authors lump together original research papers and reviews within a given group without distinguishing which is which.

We thank the reviewer for pointing this out. We reorganized the references in the introduction.

(2) One option to address the concern regarding the lack of evidence that nuclear condensates per se drive MET gene clustering is to test the impact of Met4 ΔIDR2.3 on MTAC signals.

We carried out the suggested experiment. See answer above (Reviewer #1, Question #1).

(3) Authors claim that there are significant differences between values depicted in Figures 1B and 3G. Statistical tests are necessary to show this.

Significance values were calculated in comparison to free GFP using two-tailed Student’s t-test in 1B,1C, and 3G. The corresponding figure legends are updated.

(4) How are the data in Figures 3F, G, and 6B, C generated? This is unclear from the information provided in the Figure legends and Materials and Methods.

For each cell, we projected the highest mCherry and GFP intensity at each pixel for all z positions onto a 2D plane (MIP). The MIP images were aligned with the mCherry dot at the center and averaged among all cells. To calculate the GFP intensities like in Figure 3G and 6C, a single line was drawn across the center and the GFP profile was analyzed by ImageJ. We now describe this in the corresponding figure legends, and the Materials and Methods are also updated.

(5) Typos/ unclear writing: lines 24, 58, 79, 82, 84, 96, 117, 121, 131, 142, 147, 161 (terminus, not "terminal"), 250, 325, 349, 761 (was, not "are"). For several of these: "condense" is not "condensate"; for many others: inappropriate use of "the". Supplementary Figure 1 legend: not "a single nuclei" instead "a single nucleus".

We thank the reviewer for pointing this out. We tried our best to correct grammatical errors.

(6) Define GAL1Spr (Figure 6F).

The GAL1S promoter is an attenuated GAL1 promoter that lacks two out of the four Gal4 binding site. The original paper is now cited in the manuscript on page 10.  

(7) Figure 7B, C: there appears to be an inconsistency between the image and bar graph value for ΔIDR3.

The Fano values calculated in 7C are averaged among a population of cells (we added the cell numbers to the legend), while the image in 7B is an example of an individual nucleus. There is some cell-to-cell variability in how the Met4 appears. To be more representative, we chose a different image for ΔIDR3.

(8) Supplementary Tables: use descriptive titles for file names.

This is corrected.

Reviewer #2 (Recommendations For The Authors):

Minor:

Figure 4F is not cited in the text, and the color legend seems wrong for targeted and control.

Figure 4F is now cited in the text. The labels were corrected.

Author response:

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

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

The investigators in this study analyzed the dataset assembly from 540 Salmonella isolates, and those from 45 recent isolates from Zhejiang University of China. The analysis and comparison of the resistome and mobilome of these isolates identified a significantly higher rate of cross-region dissemination compared to localized propagation. This study highlights the key role of the resistome in driving the transition and evolutionary 

Thank you for summarizing our work. According to your comments, we carefully considered and responded to them and made corresponding revisions to the text. Additionally, to fully contextualize the background knowledge and clarify the major points in this study, we add some references.

Upon further review of our initial manuscript, we realized that the original submission did not strictly follow the lineage order proposed by Zhou et al. (Natl Sci Rev. 2023 Sep 2;10(10):nwad228). To avoid confusion and keep the uniform knowledge in the typing system, we have adjusted the lineage nomenclature along the revised manuscript to reflect the corrected order as follows:

Author response table 1.

To ensure consistency with previous studies, we have revised the nomenclature for the different lineages of bvSP.

Strengths: 

The isolates included in this study were from 16 countries in the past century (1920 to 2023). While the study uses S. Gallinarun as the prototype, the conclusion from this work will likely apply to other Salmonella serotypes and other pathogens. 

Thanks for the constructive comments and the positive reception of the manuscript.

Weaknesses: 

While the isolates came from 16 countries, most strains in this study were originally from China. 

We appreciate the reviewer's observation regarding the sampling distribution of isolates in this study. We acknowledge that while the isolates were collected from 15 different countries, with a significant proportion originated from China (Author response image 1). This focus is due to several reasons:

Author response image 1.

Geographic distribution of 580 S. Gallinarum. Different colors indicate the countries of origin for the 580 S. Gallinarum strains in the dataset. Darker shades represent higher numbers of strains.

(1) As once a globally prevalent pathogen across the 20th century, S. Gallinarum was listed by the World Organization for Animal Health (WOAH) due to its economic importance. After 30 years of implementation of the National Poultry Improvement Plan in the US, it was almost eradicated in high-income countries, and interestingly, it became an endemic pathogen with sporadic outbreaks in most low- or middle-income countries like China and Brazil. Given the vast expanse of China's land area and the country's economic factors, implementing the same measures remains challenging.  

(2) S. Gallinarum is an avian-specific pathogen, particularly affecting chickens, and its distribution is closely linked to chicken meat production in different countries. There are more frequent reports of fowl typhoid in some high chicken-producing developing countries. Data from the United States Department of Agriculture (USDA) on annual chicken meat production for 2023/2024 show that the global distribution of S. Gallinarum aligns closely with the overall chicken meat production of these countries (https://fas.usda.gov/data/production/commodity/0115000).

Author response image 2.

The United States Department of Agriculture (USDA) data on annual chicken meat production for 2023/2024 across different countries globally.

(3) Our primary objective was to investigate the localized resistome adaptation of S. Gallinarum in regions. Being a region with significant disease burden, China has reported numerous outbreaks (Sci Data. 2022 Aug 13;9(1):495; Sci Data. 2024 Feb 27;11(1):244) and a high AMR prevalence of this serovar (Natl Sci Rev. 2023 Sep 2;10(10):nwad228; mSystems. 2023 Dec 21;8(6):e0088323), making it an excellent example for understanding localized resistance mechanisms.

(4) As China is the primary country of origin for the strains in this study, it is necessary to ensure that the strains from China are consistent with the local geographic characteristics of the country. Therefore, we conducted a correlation analysis between the number of strains from different provinces in China and the total GDP/population size of those provinces (Author response image 3). The results show that most points fall within the 95% confidence interval of the regression line. Although some points exhibit relative unbalance in the number of S. Gallinarum strains, most data points for these regions have a small sample size (n < 15). Overall, we found that the prevalence of S. Gallinarum in different regions of China is consistent with the overall nationwide trend.

Author response image 3.

Correlation analysis between the number of S. Gallinarum collected from different provinces in China and the total GDP/population size. The figure depicts a series of points representing individual provinces. The x-axis indicates the number of S. Gallinarum included in the dataset, while the y-axis displays the values for total GDP and total population size, respectively.

Nevertheless, a search of nearly a decade of literature on PubMed and a summary of the S. Gallinarum genome available on public databases indicate that the dataset used is the most complete. Furthermore, focusing on a specific region within China allowed us to conduct a detailed and thorough analysis. However, we highly agree that expanding the study to include more isolates from other countries would enhance the generalizability of our findings, and we are actively collecting additional S. Gallinarum genome data. In the revised manuscript, we have further emphasized the limitations as follow:

Lines 427-429: “However, the current study has some limitations. Firstly, despite assembling the most comprehensive WGS database for S. Gallinarum from public and laboratory sources, there are still biases in the examined collection. The majority (438/580) of S. Gallinarum samples were collected from China, possibly since the WGS is a technology that only became widely available in the 21st century. This makes it impractical to sequence it on a large scale in the 20th century, when S. Gallinarum caused a global pandemic. So, we suspect that human intervention in the development of this epidemic is the main driving force behind the fact that most of the strains in the data set originated in China. In our future work, we aim to actively gather more data to minimize potential biases within our dataset, thereby improving the robustness and generalizability of our findings.”

Reviewer #2 (Public review): 

Summary: 

The authors sequence 45 new samples of S. Gallinarum, a commensal Salmonella found in chickens, which can sometimes cause disease. They combine these sequences with around 500 from public databases, determine the population structure of the pathogen, and coarse relationships of lineages with geography. The authors further investigate known anti-microbial genes found in these genomes, how they associate with each other, whether they have been horizontally transferred, and date the emergence of clades. 

Thank you for your constructive suggestions, which are valuable and highly beneficial for improving our paper. According to your comments, we carefully considered and responded to them and made corresponding revisions to the text. Furthermore, to fully contextualize the background knowledge and clarify the major points in this study, we add some references to support our findings and policy implications.

Upon further review of our initial manuscript, we realized that the original submission did not strictly follow the lineage order proposed by Zhou et al. (Natl Sci Rev. 2023 Sep 2;10(10):nwad228). To avoid confusion in the typing system, we have adjusted the lineage nomenclature in the revised manuscript to reflect the corrected order (see Author response table 1).

Strengths: 

(1) It doesn't seem that much is known about this serovar, so publicly available new sequences from a high-burden region are a valuable addition to the literature. 

(2) Combining these sequences with publicly available sequences is a good way to better contextualise any findings. 

Thank you so much for your thorough review and constructive comments on the manuscript.

Weaknesses: 

There are many issues with the genomic analysis that undermine the conclusions, the major ones I identified being: 

(1) Recombination removal using gubbins was not presented fully anywhere. In this diversity of species, it is usually impossible to remove recombination in this way. A phylogeny with genetic scale and the gubbins results is needed. Critically, results on timing the emergence (fig2) depend on this, and cannot be trusted given the data presented. 

We sincerely thank you for pointing out this issue. In the original manuscript, we aimed to present different lineages of S. Gallinarum within a single phylogenetic tree constructed using BEAST. However, in the revised manuscript, we have addressed this issue by applying the approach recommended by Gubbins to remove recombination events for each lineage defined by FastBAPs. Additionally, to better illustrate the removal of recombination regions in the genome, we have included a figure generated by Gubbins (New Supplementary Figure 12). 

Our results indicate that recombination events are relatively infrequent in Lineage 1, followed by Lineage 3, but occur more frequently in Lineage 2. In the revised manuscript, we have included additional descriptions in the Methods section to clarify this analysis. We hope these modifications adequately address the reviewer’s concerns and enhance the trustworthiness of our findings.

(2) The use of BEAST was also only briefly presented, but is the basis of a major conclusion of the paper. Plot S3 (root-to-tip regression) is unconvincing as a basis of this data fitting a molecular clock model. We would need more information on this analysis, including convergence and credible intervals. 

Thank you very much for raising this issue. We decided to reconduct separate BEAST analyses for each lineage, accurately presenting the evolutionary scale based on the abovementioned improvements. The implementation of individual lineage for BEAST analysis was conducted based on the following steps:

(1) Using R51 as the reference, a reference-mapped multiple core-genome SNP sequence alignment was created, and recombination regions were detected and removed as described above.

(2) TreeTime was used to assess the temporal structure by performing a regression analysis of the root-to-tip branch distances within the maximum likelihood tree, considering the sampling date as a variable (New Supplementary Figures 6). However, the root-to-tip regression analysis presented in New Supplementary Figures 6 was not intended as a basis for selecting the best molecular clock model; its purpose was to clean the dataset with appropriate measurements.

(3) To determine the optimal model for running BEAST, we tested a total of six combinations in the initial phase of our study. These combinations included the strict clock, relaxed lognormal clock, and three population models (Bayesian SkyGrid, Bayesian Skyline, and Constant Size). Before conducting the complete BEAST analysis, we evaluated each combination using a Markov Chain Monte Carlo (MCMC) analysis with a total chain length of 100 million and sampling every 10,000 iterations. We then summarized the results using NSLogAnalyser and determined the optimal model based on the marginal likelihood value for each combination. The results indicated that the model incorporating the Bayesian Skyline and the relaxed lognormal clock yielded the highest marginal likelihood value in our sample. Then, we proceeded to perform a timecalibrated Bayesian phylogenetic inference analysis for each lineage. The following settings were configured: the "GTR" substitution model, “4 gamma categories”, the "Relaxed Clock Log Normal" model, the "Coalescent Bayesian Skyline" tree prior, and an MCMC chain length of 100 million, with sampling every 10,000 iterations.

(4) Convergence was assessed using Tracer, with all parameter effective sampling sizes (ESS) exceeding 200. Maximum clade credibility trees were generated using TreeAnnotator. Finally, key divergence time points (with 95% credible intervals) were estimated, and the tree was visualized using FigTree. 

For the key lineages, L2b and L3b (carrying the resistome, posing antimicrobial resistance (AMR) risks, and exhibiting intercontinental transmission events), we have redrawn Figure 2 based on the updated BEAST analysis results (New Figure 2). For L1, L2a, and L3c, we have added supplementary figures to provide a more detailed visualization of their respective BEAST analysis outcomes (New Supplementary Figures 3-5). The revised BEAST analysis indicates that the origin of L3b in China can be traced back to as early as 1683 (95% CI: 1608 to 1839). In contrast, the earliest possible origin of L2b in China dates back to 1880 (95% CI: 1838 to 1902). This indicates that the previous manuscript's assumption that L2b is an older lineage compared to L3b may be inaccurate. 

Furthermore, In the revised manuscript, we specifically estimated the time points for the first intercontinental transmission events for the two major lineages, L2b and L3b. Our results indicate that L2b, likely underwent two major intercontinental transmission events. The first occurred around 1893 (95% CI: 1870 to 1918), with transmission from China to South America. The second major transmission event occurred in 1923 (95% CI: 1907 to 1940), involving the spread from South America to Europe. In contrast, the transmission pattern of L3b appears relatively more straightforward. Our findings show that L3b, an S. Gallinarum lineage originating in China, only underwent one intercontinental transmission event from China to Europe, likely occurring around 1790 (95% CI: 1661 to 1890) (New Supplementary Figure 7). Based on the more critical BEAST analysis for each lineage, we have revised the corresponding conclusions in the manuscript. We believe that the updated BEAST analysis, performed using a more accurate recombination removal approach, significantly enhances the rigor and credibility of our findings.

(3) Using a distance of 100 SNPs for a transmission is completely arbitrary. This would at least need to be justified in terms of the evolutionary rate and serial interval. 

Using single nucleotide polymorphism (SNP) distance to trace pathogen transmission is a common approach (J Infect Dis. 2015 Apr 1;211(7):1154-63) and in our previous studies (hLife 2024; 2(5):246-256. mLife 2024; 3(1):156-160.). When the SNP distance within a cluster falls below a set threshold, the strains in that cluster are considered to have a potential direct transmission link. It is generally accepted that the lower the threshold, the more stringent the screening process becomes. However, there is little agreement in the literature regarding what such a threshold should be, and the appropriate SNP cut-off for inferring transmission likely depends critically on the context (Mol Biol Evol. 2019 Mar 1;36(3):587-603).

In this study, we compared various thresholds (SNPs = 5, 10, 20, 25, 30, 35, 40, 50, 100) to ensure clustering in an appropriate manner. First, we summarized the tracing results under each threshold (Author response image 4), which demonstrated that, regardless of the threshold used, all strains associated with transmission events originated from the same location (New Figure 3a).

Author response image 4.

Clustering results of 45 newly isolated S. Gallinarum strains using different SNP thresholds of 5, 10, 15, 20, 25, 28, 30, 50, and 100 SNPs. The nine subplots represent the clustering results under each threshold. Each point corresponds to an individual strain, and lines connect strains with potential transmission relationships.

In response to your comments regarding the evolutionary rate, we estimated the overall evolutionary rate of the S. Gallinarum using BEAST. We applied the methodology described by Arthur W. Pightling et al. (Front Microbiol. 2022 Jun 16; 13:797997). The numbers of SNPs per year were determined by multiplying the evolutionary rates estimated with BEAST by the number of core SNP sites identified in the alignments. We hypothesize that a slower evolutionary rate in bacteria typically requires a lower SNP threshold when tracing transmission events using SNP distance analysis. Pightling et al.'s previous research found an average evolutionary rate of 1.97 SNPs per year (95% HPD, 0.48 to 4.61) across 22 different Salmonella serotypes. Our updated BEAST estimation for the evolutionary rate of S. Gallinarum suggests it is approximately 0.74 SNPs per year (95% HPD, 0.42 to 1.06). Based on these findings, and our previous experience with similar studies (mBio. 2023 Oct 31;14(5):e0133323.), we set a threshold of 5 SNPs in the revised manuscript.

Then, we adopted the newly established SNP distance threshold (n=5) to update Figure 3a and New Supplementary Figure 8. The heatmap on the far right of New Figure 3a illustrates the SNP distances among 45 newly isolated S. Gallinarum strains from two locations in Zhejiang Province (Taishun and Yueqing). New Supplementary Figure 8 simulates potential transmission events between the bvSP strains isolated from Zhejiang Province (n=95) and those from China with available provincial information (n=435). These analyses collectively demonstrate the localized transmission pattern of bvSP within China. Our analysis using the newly established SNP threshold indicates that the 45 strains isolated from Taishun and Yueqing exhibit a highly localized transmission pattern, with pairs of strains exhibiting potential transmission events below the set threshold occurring exclusively within a single location. Subsequently, we conducted the SNP distance-based tracing analysis for the 95 strains from Zhejiang Province and those from China with available provincial information (n=435) (New Supplementary Figure 8, New Supplementary Table S8). Under the SNP distance threshold (n=5), we identified a total of 91 potential transmission events, all of which occurred exclusively within Zhejiang Province. No inter-provincial transmission events were detected. Based on these findings, we revised the methods and conclusions in the manuscript accordingly. We believe that the updated version well addresses your concerns.

Nevertheless, the final revised and updated results do not change the conclusions presented in our original manuscript. Instead, applying a more stringent SNP distance threshold allows us to provide solid evidence supporting the localized transmission pattern of S. Gallinarum in China. 

(4) The HGT definition is non-standard, and phylogeny (vertical inheritance) is not controlled for.  

The cited method: 

'In this study, potentially recently transferred ARGs were defined as those with perfect identity (more than 99% nucleotide identity and 100% coverage) in distinct plasmids in distinct host bacteria using BLASTn (E-value {less than or equal to}10−5)' 

This clearly does not apply here, as the application of distinct hosts and plasmids cannot be used. Subsequent analysis using this method is likely invalid, and some of it (e.g. Figure 6c) is statistically very poor. 

Thank you for raising this important question. In our study, Horizontal Gene Transfer (HGT) is defined as the transfer of genetic information between different organisms, a process that facilitates the spread of antibiotic resistance genes (ARGs) among bacteria. This definition of HGT is consistent with that used in previous studies (Evol Med Public Health. 2015; 2015(1):193–194; ISME J. 2024 Jan 8;18(1):wrad032). In Salmonella, the transfer of antimicrobial resistance genes via HGT is not solely dependent on plasmids; other mobile genetic elements (MGEs), such as transposons, integrons, and prophages, also play significant roles. This has also  been documented in our previous work (mSystems. 2023 Dec 21;8(6):e0088323). Given the involvement of various MGEs in the horizontal transfer of ARGs, we propose that the criteria for evaluating horizontal transfer via plasmids can also be applied to ARGs mediated by other MGEs.

In this study, we adopted stricter criteria than those used by Xiaolong Wang et al. Specifically, we defined two ARGs as identical only if they exhibited 100% nucleotide identity and 100% coverage. To address concerns regarding the potential influence of vertical inheritance in our analysis, we have made the following improvements. In the revised manuscript, we provide a more detailed table that includes the co-localization analysis of each ARG with mobile genetic elements (New Supplementary Table 9). For prophages and plasmids, we required that ARGs be located directly within these elements. In contrast, for transposons and integrons, we considered ARGs to be associated if they were located within a 5 kb region upstream or downstream of these elements (Nucleic Acids Res. 2022 Jul 5;50(W1):W768-W773). 

In the revised manuscript, we first categorized a total of 621 ARGs carried by 436 bvSP isolates collected in China according to the aforementioned criteria and found that 415 ARGs were located on MGEs. After excluding the ARGs not associated with MGEs, we recalculated the overall HGT frequency of 10 types of ARGs in China, the horizontal ARGs transfer frequency in three key regions, and the horizontal ARGs transfer frequency within a single region (New Supplementary Table 7). Based on the results, we updated relevant sections of the manuscript and remade Figure 6. The updated manuscript describes the results of this section as follows:

“Horizontal transfer of resistome occurs widely in localized bvSP

Horizontal transfer of the resistome facilitates the acquisition of AMR among bacteria, which may record the distinct acquisition event in the bacterial genome. To compare these events in a geographic manner, we further investigated the HGT frequency of each ARG carried by bvSP isolated from China and explored the HGT frequency of resistome between three defined regions. Potentially horizontally transferred ARGs were defined as those with perfect identity (100% identity and 100% coverage) and were located on MGEs across different strains (Fig. 6a). We first categorized a total of 621 ARGs carried by 436 bvSP isolates collected in China and found that 415 ARGs were located on MGEs. After excluding the ARGs not associated with MGEs, our findings reveal that horizontal gene transfer of ARGs is widespread among Chinese bvSP isolates, with an overall transfer rate of 92%. Specifically, 50% of the ARGs exhibited an HGT frequency of 100%, indicating that these ARGs might underwent extensive frequent horizontal transfer events (Fig. 6b). It is noteworthy that certain resistance genes, such as tet(A), aph(3'')-Ib, and aph(6)-Id, appear to be less susceptible to horizontal transfer.

However, different regions generally exhibited a considerable difference in resistome HGT frequency. Overall, bvSP from the southern areas in China showed the highest HGT frequency (HGT frequency=95%). The HGT frequencies for bvSP within the eastern and northern regions of China are lower, at 92% and 91%, respectively (Fig. 6c). For specifical ARG type, we found tet(A) is more prone to horizontal transfer in the southern region, and this proportion was considerably lower in the eastern region. Interestingly, certain ARGs such as aph(6)-Id, undergo horizontal transfer only within the eastern and northern regions of China (Fig. 6d). Notably, as a localized transmission pathogen, resistome carried by bvSP exhibited a dynamic potential among inter-regional and local demographic transmission, especially from northern region to southern region (HGT frequency=93%) (Fig. 6e, Supplementary Table 7).”

We also modified the current version of the pipeline used to calculat the HGT frequency of resistance genes. In the revised pipeline, users are required to provide a file specifying the locations of mobilome on the genome before formally calculating the HGT frequency of the target ARGs. The specific code and data used in the calculation have been uploaded to https://github.com/tjiaa/Cal_HGT_Frequency.

However, we also acknowledge that the current in silico method has some limitations. This approach heavily relies heavily on prior information in existing resistome/mobilome databases. Additionally, the characteristics of second-generation sequencing data make it challenging to locate gene positions precisely. Using complete genome assemblies might be a crucial approach to address this issue effectively. In the revised manuscript, we have also provided a more detailed explanation of the implications of the current pipeline.

Regarding your second concern, "some of it (e.g., Figure 6c) is statistically very poor," the horizontal ARG transfer frequency calculation for each region was based on the proportion of horizontal transfer events of ARGs in that region to the total possible transfer events. As a result, we are unable to calculate the statistical significance between the two regions. Our aim with this approach is to provide a rough estimate of the extent of horizontal ARG transfer within the S. Gallinarum population in each region. In future studies, we will refine our conclusions by developing a broader range of evaluation methods to ensure more comprehensive assessment and validation.

(5) Associations between lineages, resistome, mobilome, etc do not control for the effect of genetic background/phylogeny. So e.g. the claim 'the resistome also demonstrated a lineage-preferential distribution' is not well-supported. 

Thank you for your comments. We acknowledge that the associations between lineages and the mobilome/resistome may be influenced by the genetic background or phylogeny of the strains. For instance, our conclusion regarding the lineage-preferential distribution of the resistome was primarily based on New Figure 4a, where L3 is clearly shown to carry the most ARGs. Furthermore, we observed that L3b tends to harbor bla_{_TEM-1B}, _sul2, and tet(A) more frequently than other lineages. However, we recognize that this evidence is insufficient to support a definitive conclusion of “demonstrated a lineage-preferential distribution”. Therefore, we have re-examined the current manuscript and described these findings as a potential association between the mobilome/resistome and lineages.

(6) The invasiveness index is not well described, and the difference in means is not biologically convincing as although it appears significant, it is very small. 

Thank you for pointing this out. For the invasiveness index mentioned in the manuscript, we used the method described in previous studies. (PLoS Genet. 2018 May 8;14(5), Nat Microbiol. 2021 Mar;6(3):327-338). Specifically, Salmonella’s ability to cause intestinal or extraintestinal infections in hosts is related to the degree of genome degradation. We evaluated the potential for extraintestinal infection by 45 newly isolated S. Gallinarum strains (L2b and L3b) using a model that quantitatively assesses genome degradation. We analyzed samples using the 196 top predictor genes, employing a machine-learning approach that utilizes a random forest classifier and delta-bitscore functional variant-calling. This method evaluated the invasiveness of S. Gallinarum towards the host, and the distribution of invasiveness index values for each region was statistically tested using unpaired t-test. The code used for calculating the invasiveness index is available at https://github.com/Gardner-BinfLab/invasive_salmonella. In the revised manuscript, we added a more detailed description of the invasiveness index calculation in the Methods section as follows:

Lines 592-603: “Specifically, Salmonella’s ability to cause intestinal or extraintestinal infections in hosts is related to the degree of genome degradation. We evaluated the potential for extraintestinal infection by 45 newly isolated S. Gallinarum strains (L2b and L3b) using a model that quantitatively assesses genome degradation. We analyzed each sample using the 196 top predictor genes for measuring the invasiveness of S. Gallinarum, employing a machine-learning approach that utilizes a random forest classifier and deltabitscore functional variant-calling. This method evaluated the invasiveness of S. Gallinarum towards the host, and the distribution of invasiveness index values for each region was statistically tested using unpaired t-test. The code used for calculating the invasiveness index is available at: https://github.com/Gardner-BinfLab/invasive_salmonella.”

Regarding the second question, 'the difference in means is not biologically convincing as although it appears significant, it is very small,' we believe that this difference is biologically meaningful. In our previous work, we infected chicken embryos with different lineages of S. Gallinarum (Natl Sci Rev. 2023 Sep 2;10(10):nwad228). The virulence of thirteen strains of Salmonella Gallinarum, comprising five from lineage L2b and eight from lineage L3b, was evaluated in 16-day-old SPF chicken embryos through inoculation into the allantoic cavity. Controls included embryos that inoculated with phosphate-buffered saline (PBS). The embryos were incubated in a thermostatic incubator maintained at 37.5°C with a relative humidity ranging from 50% to 60%. Prior to inoculation, the viability of the embryos was assessed by examining the integrity of their venous system and their movements; any dead embryos were excluded from the study. Overnight cultures resuspended in PBS at a concentration of 1000 CFU per 100 μL were administered to the embryos. Mortality was recorded daily for a period of five days, concluding upon the hatching of the chicks. 

It is generally accepted that strains with higher invasive capabilities are more likely to cause chicken embryo mortality. Our experimental results showed that the L2b, which exhibits higher invasiveness, with a slightly higher to cause chicken embryo death (Author response image 5). 

Author response image 5.

The survival curves of chicken embryos infected with bvSP isolates from S. Gallinarum L2b and S. Gallinarum L3b. Inoculation with Phosphate Buffer Saline (PBS) were considered controls. 

(7) 'In more detail, both the resistome and mobilome exhibited a steady decline until the 1980s, followed by a consistent increase from the 1980s to the 2010s. However, after the 2010s, a subsequent decrease was identified.' 

Where is the data/plot to support this? Is it a significant change? Is this due to sampling or phylogenetics? 

Thank you for highlighting these critical points. The description in this statement is based on New Supplementary Figure 11. On the right side of New Supplementary Figure 11, we presented the average number of Antimicrobial Resistance Genes (ARGs) and Mobile Genetic Elements (MGEs) carried by S. Gallinarum isolates from different years, and we described the overall trend across these years. However, we realized that this statement might overinterpret the data. Given that this sentence does not impact our emphasis on the overall increasing trends observed in the resistome and mobilome, as well as their potential association, we decided to remove it in the revised manuscript.

The revised paragraph would read as follows:

Lines 261-268: “Variations in regional antimicrobial use may result in uneven pressure for selecting AMR. The mobilome is considered the primary reservoir for spreading resistome, and a consistent trend between the resistome and the mobilome has been observed across different lineages, from L1-L3c. We observed an overall gradual rise in the resistome quantity carried by bvSP across various lineages, correlating with the total mobilome content (S11 Fig). Furthermore, we investigated the interplay between particular mobile elements and resistome types in bvSP.”

(8) It is not clear what the burden of disease this pathogen causes in the population, or how significant it is to agricultural policy. The article claims to 'provide valuable insights for targeted policy interventions.', but no such interventions are described. 

Thank you for your constructive suggestions. Salmonella Gallinarum is an avian-specific pathogen that induces fowl typhoid, a severe systemic disease characterized by high mortality rates in chickens, thereby posing a significant threat to the poultry industry, particularly in developing countries (Rev Sci Tech. 2000 Aug;19(2):40524). In our previous research, we conducted a comprehensive meta-analysis of 201 publications encompassing over 900 million samples to investigate the global impact of S. Gallinarum (Sci Data. 2022 Aug 13;9(1):495). Our findings estimated that the global prevalence of S. Gallinarum is 8.54% (with a 95% confidence interval of 8.43% to 8.65%), with notable regional variations in incidence rates.

Our previously analysis focused on the prevalence of S. Gallinarum (including biovars SP and SG) across six continents. The results revealed that all continents, except Oceania, exhibited positive prevalences of S. Gallinarum. Asia had the highest prevalence at 17.31%, closely followed by Europe at 16.03%. In Asia, the prevalence of biovar SP was higher than that of biovar SG, whereas in Europe, biovar SG was observed to be approximately two hundred times more prevalent than biovar SP. In South America, the prevalence of S. Gallinarum was higher than that of biovar SP, at 10.06% and 13.20% respectively. Conversely, the prevalence of S. Gallinarum was relatively lower in North America (4.45%) compared to Africa (1.10%) (Author response image 6).

Given the significant economic losses caused by S. Gallinarum to the poultry industry and the potential risk of escalating antimicrobial resistance, more targeted policy interventions are urgently needed. Further elaboration on this implication is provided in the revised “Discussion” section as follows:

Lines 401-416: “In summary, the findings of this study highlight that S. Gallinarum remains a significant concern in developing countries, particularly in China. Compared to other regions, S. Gallinarum in China poses a notably higher risk of AMR, necessitating the development of additional therapies, i.e. vaccine, probiotics, bacteriophage therapy in response to the government's policy aimed at reducing antimicrobial use ( J Infect Dev Ctries. 2014 Feb 13;8(2):129-36). Furthermore, given the dynamic nature of S. Gallinarum risks across different regions, it is crucial to prioritize continuous monitoring in key areas, particularly in China's southern regions where the extensive poultry farming is located. Lastly, from a One-Health perspective, controlling AMR in S. Gallinarum should not solely focus on local farming environments, with improved overall welfare on poultry and farming style. The breeding pyramid of industrialized poultry production should be targeted on the top, with enhanced and accurate detection techniques (mSphere. 2024 Jul 30;9(7):e0036224). More importantly, comprehensive efforts should be made to reduce antimicrobial usage overall and mitigate potential AMR transmission from environmental sources or other hosts (Vaccines (Basel). 2024 Sep 18;12(9):1067; Vaccines (Basel). 2023 Apr 18;11(4):865; Front Immunol. 2022 Aug 11:13:973224).”

Author response image 6.

A comparison of the global prevalence of S. gallinarum across continents.

(9) The abstract mentions stepwise evolution as a main aim, but no results refer to this. 

Thank you for raising this issue. In the revised manuscript, we have changed “stepwise evolution” to simply “evolution” to ensure a more accurate and precise description.

(10) The authors attribute changes in population dynamics to normalisation in China-EU relations and hen fever. However, even if the date is correct, this is not a strongly supported causal claim, as many other reasons are also possible (for example other industrial processes which may have changed during this period). 

Thank you for raising this critical issue. In the revised manuscript, we conducted a more stringent BEAST analysis for each lineage, as described earlier. This led to some changes in the inferred evolutionary timelines. Consequently, we have removed the corresponding statement from the “Results” section. Instead, we now only provide a discussion of historical events, supported by literature, that could have facilitated the intercontinental spread of L2b and L3b in the “Discussion” section. We believe these revisions have made the manuscript more rigorous and precise.

Lines 332-342: “_The biovar types of _S. Gallinarum have been well-defined as bvSP, bvSG, and bvSD historically ( J Vet Med B Infect Dis Vet Public Health. 2005 Jun;52(5):2148). Among these, bvSP can be further subdivided into five lineages (L1, L2a, L2b, L3b, and L3c) using hierarchical Bayesian analysis. Different sublineages exhibited preferential geographic distribution, with L2b and L3b of bvSP being predominant global lineage types with a high risk of AMR. The historical geographical transmission was verified using a spatiotemporal Bayesian framework. The result shows that L3b was initially spread from China to Europe in the 18^th-19^th century, which may be associated with the European hen fever event in the mid-19th century (Burnham GP. 1855. The history of the hen fever: a humorous record). L2b, on the other hand, appears to have spread to Europe via South America, potentially contributing to the prevalence of bvSP in the United States.”  

(11) No acknowledgment of potential undersampling outside of China is made, for example, 'Notably, all bvSP isolates from Asia were exclusively found in China, which can be manually divided into three distinct regions (southern, eastern, and northern).'.

Perhaps we just haven't looked in other places?

We appreciate the reviewer's observation regarding the sampling distribution of isolates in this study. We acknowledge that while the isolates were collected from 15 different countries with, a significant proportion originated from China (Author response image 1). This focus is due to several reasons:

(1) As once a globally prevalent pathogen across the 20th century, S. Gallinarum was listed by the World Organization for Animal Health (WOAH) due to its economic importance. After 30 years of implementation the National Poultry Improvement Plan in the US, it was almost eradicated in high-income countries, and interestingly, it became an endemic pathogen with sporadic outbreaks in most low- or middle-income countries like China and Brazil. Given the vast expanse of China's land area and the country's economic factors, implementing the same measures remains a challenging endeavour. 

(2) S. Gallinarum is an avian-specific pathogen, particularly affecting chickens, and its distribution is closely linked to chicken meat production in different countries. In some high chicken-producing developing countries, such as China and Brazil, there are more frequent reports of fowl typhoid. Data from the United States Department of Agriculture (USDA) on annual chicken meat production for 2023/2024 show that the global distribution of S. Gallinarum aligns closely with the overall chicken meat production of these countries (https://fas.usda.gov/data/production/commodity/0115000).  

(3) Our primary objective was to investigate the localized resistome adaptation of S. Gallinarum in regions. Being a region with significant disease burden, China has reported numerous outbreaks (Sci Data. 2022 Aug 13;9(1):495; Sci Data. 2024 Feb 27;11(1):244) and a high AMR prevalence of this serovar (Natl Sci Rev. 2023 Sep 2;10(10):nwad228; mSystems. 2023 Dec 21;8(6):e0088323), making it an excellent example for understanding localized resistance mechanisms. 

Nevertheless, a search of nearly a decade of literature on PubMed and a summary of the S. Gallinarum genome available on public databases indicate that the dataset used is the most complete. Furthermore, focusing on a specific region within China allowed us to conduct a detailed and thorough analysis. However, we highly agree that expanding the study to include more isolates from other countries would enhance the generalizability of our findings, and we are actively collecting additional S. Gallinarum genome data. In the revised manuscript, we modified this sentence to indicate that this phenomenon is only observed in the current dataset, thereby avoiding an overly absolute statement:

Lines 131-135: “For the bvSP strains from Asia included in our dataset, we found that all originated from China. To further investigate the distribution of bvSP across different regions in China, we categorized them into three distinct regions: southern, eastern, and northern (Supplementary Table 3)”.

(12) Many of the conclusions are highly speculative and not supported by the data. 

Thank you for your comment. We have carefully revised the manuscript to address your concerns. We hope that the changes made in the revised version meet your expectations and provide a clearer and more accurate interpretation of our findings.

(13) The figures are not always the best presentation of the data: 

a. Stacked bar plots in Figure 1 are hard to interpret, the total numbers need to be shown.

Panel C conveys little information. 

b. Figure 4B: stacked bars are hard to read and do not show totals. 

c. Figure 5 has no obvious interpretation or significance. 

Thank you for your comments. We have revised the figures to improve the clarity and presentation of the data.

In summary, the quality of analysis is poor and likely flawed (although there is not always enough information on methods present to confidently assess this or provide recommendations for how it might be improved). So, the stated conclusions are not supported. 

Thank you for your valuable feedback. We have carefully revised the manuscript to address your concerns. We hope that the updated figures and tables, and new data in the revised version meet your expectations and provide more appropriate interpretation of our findings.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors): 

This reviewer enjoyed reading this well-written manuscript. The authors are encouraged to address the following comments and revise the manuscript accordingly. 

(1) Title: The authors use avian-restrict Salmonella to refer to Salmonella Gallinarum. Please consider using Salmonella Gallinarum in the title. Also, your analysis relates to resistome and mobilome. Would it make sense to add mobilome in the manuscript? 

Thank you for your guidance. In the revised manuscript, we have changed the title to “Avian-specific Salmonella enterica Serovar Gallinarum transition to endemicity is accompanied by localized resistome and mobilome interaction”. We believe that this revised title more accurately reflects the content of our study.

(2) Abstract: This study uses 45 isolates from your labs. However, you failed to include these 45 isolates in the Abstract. Also, please clarify the sources of these isolates (from dead chickens, or dead chicken embryos? You wrote in two different ways in this manuscript). Also, I am not entirely convinced how the results from these 45 isolates will support the overall conclusion of this work. 

Thank you for your thorough review and constructive comments on the manuscript. In the revised version, we have added a description of 45 newly isolated S. Gallinarum strains in the Abstract to provide readers with a clearer understanding of the dataset used in this study.

Lines 36-41: “Using the most comprehensive whole-genome sequencing dataset of Salmonella enterica serovar Gallinarum (S. Gallinarum) collected from 16 countries, including 45 newly recovered samples from two related local regions, we established the relationship among avian-specific pathogen genetic profiles and localization patterns.”

Furthermore, the newly isolated S. Gallinarum strains were obtained from dead chicken embryos. We think your second concern may arise from the following description in the manuscript: “All 734 samples of dead chicken embryos were collected from Taishun and Yueqing in Zhejiang Province, China. After the thorough autopsy, the liver, intestines, and spleen were extracted and added separately into 2 mL centrifuge tubes containing 1 mL PBS. The organs were then homogenized by grinding.” In fact, all the collected dead chicken embryos were aged 19 to 20 days. At this developmental stage, collecting the liver, intestines, and spleen for isolation and cultivation of S. Gallinarum is possible. To avoid any confusion, we have included a more detailed description of the dead chicken embryos in the revised manuscript as follows:

Lines 447-451: “All 734 samples of dead chicken embryos aged 19 to 20 days were collected from Taishun and Yueqing in Zhejiang Province, China. After a thorough autopsy, the liver, intestines, and spleen were extracted and added separately into 2 mL centrifuge tubes containing 1 mL PBS. The organs were then homogenized by grinding.”

Regarding your concern about the statement, “I am not entirely convinced how the results from these 45 isolates will support the overall conclusion of this work,” we would like to clarify the significance of these new isolates. Our research first identified distinct characteristics in the 45 newly isolated S. Gallinarum strains from Taishun and Yueqing, Zhejiang Province. Specifically, we found that most of the strains from Yueqing belonged to sequence type ST92, whereas the majority from Taishun were ST3717. Additionally, there were significant differences between these geographically close strains in terms of SNP distance and predicted invasion capabilities. These findings suggest that S. Gallinarum may exhibit localized transmission patterns, which forms the basis of the scientific question and hypothesis we originally aimed to address. Furthermore, in our previous work, we collected 325 S. Gallinarum strains. By incorporating the newly isolated 45 strains, we aim to provide a more comprehensive view of the population diversity, transmission pattern and potential risk of S. Gallinarum. We will continue to endeavour to understand the global genomic and population diversity in this field.

Finally, we revised the sentences that could potentially raise concerns for readers: 

Lines 175-177: “To investigate the dissemination pattern of bvSP in China, we obtained forty-five newly isolated bvSP from 734 samples (6.1% overall isolation rate) collected from diseased chickens at two farms in Yueqing and Taishun, Zhejiang Province.”  >  “To investigate the dissemination pattern of bvSP, we obtained forty-five newly isolated bvSP from 734 samples (6.1% overall isolation rate) collected from diseased chickens at two farms in Yueqing and Taishun, Zhejiang Province.”

(3) The manuscript uses nomenclature and classification into different sublineages. Did the authors establish the approaches for defining these sublineages in this group or did you follow the accepted standards? 

Thank you very much for raising this important issue. The biovar types of Salmonella Gallinarum have historically been well-defined as S. Gallinarum biovar

Pullorum (bvSP), S. Gallinarum biovar Gallinarum (bvSG), and S. Gallinarum biovar Duisburg (bvSD) (J Vet Med B Infect Dis Vet Public Health. 2005 Jun;52(5):214-8). However, there seems to be no widespread consensus on the population nomenclature for the key biovar bvSP. In a previous study, Zhou et al. classified bvSP into six lineages:

L1, L2a, L2b, L3a, L3b, and L3c (Natl Sci Rev. 2023 Sep 2;10(10):nwad228). However, our more comprehensive analysis of S. Gallinarum using a larger dataset and hierarchical Bayesian clustering revealed that L3a, previously considered a distinct lineage, is actually a sublineage of L3c. Upon further review of our initial manuscript, we realized that the original submission did not strictly follow the lineage order proposed by Zhou et al. To avoid confusion in the typing system, we have adjusted the lineage nomenclature in the revised manuscript to reflect the corrected order (see Author response table 1).

(4) This reviewer is convinced with the analysis approaches and conclusion of this work.

In the meantime, the authors are encouraged to discuss the application of the conclusion of this study: a) can the data be somehow used in the prediction model? b) would the conclusion from S. Gallinarum have generalized application values for other pathogens. 

Thank you for your constructive comments on the manuscript. 

a) can the data be somehow used in the prediction model?

We believe that genomic data can be effectively used for constructing prediction models; however, the success of such models largely depends on the specific traits being predicted. In this study, we utilized a random forest prediction model based on 196 top genes (PLoS Genet. 2018 May 8;14(5)) to predict the invasiveness of 45 newly isolated strains. In relation to the antimicrobial resistance (AMR) issue discussed in this paper, we also conducted relevant analyses. For instance, we explored the use of image-based models to predict whether a genome is resistant to specific antibiotics (Comput Struct Biotechnol J. 2023 Dec 29:23:559-565). We are confident that the incorporation of newly generated data will facilitate the development of future predictive models, and we plan to pursue further research in this area.

b) would the conclusion from S. Gallinarum have generalized application values for other pathogens.

This might be explained from two perspectives. First, the key role of the mobilome in facilitating the spread of the resistome, as emphasized in this study, has also been confirmed in research on other pathogens (mBio. 2024 Oct 16;15(10):e0242824). Thus, we believe that the pipeline we developed to assess the horizontal transfer frequency of different resistance genes across regions applies to various pathogens. On the other hand, due to distinct evolutionary histories, different pathogens exhibit varying levels of adaptation to their environments. In this study, we found that S. Gallinarum tends to spread highly localized; however, this conclusion may not necessarily hold for other pathogens.

Reviewer #2 (Recommendations for the authors): 

The authors would need to: 

(1) Address my concerns about genomic analyses listed in the public review. 

Thank you for your valuable feedback. We have carefully reviewed your concerns and made the necessary revisions to address the points raised about genomic analyses in the public review. We sincerely hope that these modifications meet your expectations and provide more robust analysis. We appreciate your thoughtful input and remain open to further suggestions to improve the manuscript.

(2) Add more detail on the genomic methods and their outputs, as suggested above. 

We have added further details to clarify the methodologies and outputs as mentioned above. Specifically, we expanded the description of the data processing, and the bioinformatic tools used for analysis. To ensure clarity, we also included an expanded discussion of the key outputs, highlighting their implications. We hope these revisions meet your expectations.

(3) Critically rewrite their introduction to make it clear what problem they are trying to address. 

Thank you for your guidance. In the revised manuscript, we have made the necessary modifications to the Introduction section to more clearly articulate the problem we aim to address.

(4) Critically rewrite their conclusions so they are supported by the data they present, and make it clear when claims are more speculative. 

Thank you for your guidance. In the revised manuscript, we have made the recommended modifications to the relevant sections of the conclusion as outlined above.

More minor issues I identified: 

(1) Typo in the title 'avian-restrict'. 

Done.

Line 1: “Avian-specific Salmonella enterica Serovar Gallinarum transition to endemicity is accompanied by localized resistome and mobilome interaction.”

(2) 'By utilizing the pipeline we developed' -- a pipeline has not been introduced at this point. 

In the revised manuscript, we have removed this section from the 'Abstract'.

Lines 46-48: “Notably, the mobilome-resistome combination among distinct lineages exhibits a geographical-specific manner, further supporting a localized endemic mobilome-driven process.”

(3) 'has more than 90% serovars' -- doesn't make sense. 

Revised.

Lines 82-83: “Salmonella, a pathogen with distinct geographical characteristics, has more than 90% of its serovars frequently categorized as geo-serotypes.”

(4) 'horrific mortality rates that remain a disproportionate burden'. 

Revised.

Lines 83-87: “Among the thousands of geo-serotypes, Salmonella enterica Serovar Gallinarum (S. Gallinarum) is an avian-specific pathogen that causes severe mortality, with particularly detrimental effects on the poultry industry in low- and middle-income countries.”

(5) What is the rate, what is a comparison, how is it disproportionate? 

Thank you for your valuable feedback. It is challenging to accurately estimate the specific prevalence of S. Gallinarum, particularly due to the lack of comprehensive data in many countries. Numerous cases likely go unreported. However, S. Gallinarum is more commonly detected in low- and middle-income countries. Here, we provide three evidence supporting this observation. First, in our previous research, we conducted a comprehensive meta-analysis of 201 studies, involving over 900 million samples, to evaluate the global impact of S. Gallinarum (Sci Data. 2022 Aug 13;9(1):495). The estimated prevalence in 17 countries showed that Bangladesh had the highest rate (25.75%) of S. Gallinarum infections. However, for biovar Pullorum (bvSP), Argentina (20.69%) and China (18.18%) reported the highest prevalence rates. Second, previous studies have also reported that S. Gallinarum predominantly occurs in low- and middleincome countries (Vet Microbiol. 2019 Jan:228:165-172; BMC Microbiol. 2024 Oct 18;24(1):414). Finally, S. Gallinarum was once a globally prevalent pathogen in the 20th century. Following the implementation of eradication programs in most high-income countries, it was listed by the World Organization for Animal Health and subsequently became an endemic pathogen with sporadic outbreaks. However, similar eradication efforts are challenging to implement in low- and middle-income countries, leading to a disproportionately higher incidence of S. Gallinarum in these regions.

In the revised manuscript, we have rephrased this sentence to enhance its accuracy:

Lines 83-87: “Among the thousands of geo-serotypes, Salmonella enterica serovar Gallinarum (S. Gallinarum) is an avian-specific pathogen that causes severe mortality, with particularly detrimental effects on the poultry industry in low- and middle-income countries.”

(6) 'we collected the most comprehensive set of 580 S. Gallinarum isolates', -> 'we collected the most comprehensive set S. Gallinarum isolates, consisting of 580 genomes'. 

Revised.

Lines 97-100: “To fill the gaps in understanding the evolution of S. Gallinarum under regional-associated AMR pressures and its adaptation to endemicity, we collected the most comprehensive set S. Gallinarum isolates, consisting of 580 genomes, spanning the period from 1920 to 2023.” 

(7) Sequence reads are not available, and use a non-standard database. The eLife policy states: 'Sequence reads and assembly must be included for reference genomes, while novel short sequences, including epitopes, functional domains, genetic markers and haplotypes should be deposited, together with surrounding sequences, into Genbank, DNA Data Bank of Japan (DDBJ), or EMBL Nucleotide Sequence Database (ENA). DNA and RNA sequencing data should be deposited in NCBI Trace Archive or NCBI Sequence Read Archive (SRA).' So the sequences assemblies and reads should ideally be mirrored appropriately. 

Thank you for your valuable suggestion regarding submitting the genome data for the newly isolated 45 S. Gallinarum strains. The genome data have been deposited in the NCBI Sequence Read Archive (SRA) under two BioProjects. The “SRA Accession number” for each strain have been added to New Supplementary Table 1. We believe this will ensure that the data are more readily accessible to a broader audience of researchers for download and analysis. We have revised the corresponding paragraph in the manuscript as follows:

Lines 606-608: “For the newly isolated 45 strains of Salmonella Gallinarum, genome data have been deposited in NCBI Sequence Read Archive (SRA) database. The “SRA Accession” for each strain are listed in Supplementary Table 1.”

(8) You should state at the start of the results which data is public, and how much is newly sequenced. 

Revised.

Lines 109-112: “To understand the global geographic distribution and genetic relationships of S. Gallinarum, we assembled the most comprehensive S. Gallinarum WGS dataset (n=580), comprising 535 publicly available genomes and 45 newly sequenced genomes.”

Author Response:

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

Reviewer #1 (Public Review):

Chan et al. tried identifying the binding sites or pockets for the KCNQ1-KCNE1 activator mefenamic acid. Because the KCNQ1-KCNE1 channel is responsible for cardiac repolarization, genetic impairment of either the KCNQ1 or KCNE1 gene can cause cardiac arrhythmia. Therefore, the development of activators without side effects is highly demanded. Because the binding of mefenamic acid requires both KCNQ1 and KCNE1 subunits, the authors performed drug docking simulation by using KCNQ1-KCNE3 structural model (because this is the only available KCNQ1-KCNE structure) with substitution of the extracellular five amino acids (R53-Y58) into D39-A44 of KCNE1. That could be a limitation of the work because the binding mode of KCNE1 might differ from that of KCNE3. Still, they successfully identified some critical amino acid residues, including W323 of KCNQ1 and K41 and A44 of KCNE1. They subsequently tested these identified amino acid residues by analyzing the point mutants and confirmed that they attenuated the effects of the activator. They also examined another activator, yet structurally different DIDS, and reported that DIDS and mefenamic acid share the binding pocket, and they concluded that the extracellular region composed of S1, S6, and KCNE1 is a generic binding pocket for the IKS activators.

The data are solid and well support their conclusions, although there are a few concerns regarding the choice of mutants for analysis and data presentation.

Other comments:

1. One of the limitations of this work is that they used psKCNE1 (mostly KCNE3), not real KCNE1, as written above. It is also noted that KCNQ1-KCNE3 is in the open state. Unbinding may be facilitated in the closed state, although evaluating that in the current work is difficult.

We agree that it is difficult to evaluate the role of unbinding from our model. Our data showing that longer interpulse intervals have a normalizing effect on the GV curve (Figure 3-figure supplement 2) could be interpreted to suggest that unbinding occurs in the closed state. Alternatively, the slowing of deactivation caused by S1-S6 interactions and facilitated by the activators may effectively be exceeded at the longer interpulse intervals.

1. According to Figure 2-figure supplement 2, some amino acid residues (S298 and A300) of the turret might be involved in the binding of mefenamic acid. On the other hand, Q147 showing a comparable delta G value to S298 and A300 was picked for mutant analysis. What are the criteria for the following electrophysiological study?

EP experiments interrogated selected residues with significant contributions to mefenamic acid and DIDs coordination as revealed by the MM/GBSA and MM/PBSA methods. A300 was identified as potentially important. We did attempt A300C but were never able to get adequate expression for analysis.

1. It is an interesting speculation that K41C and W323A stabilize the extracellular region of KCNE1 and might increase the binding efficacy of mefenamic acid. Is it also the case for DIDS? K41 may not be critical for DIDS, however.

Yes, we found K41 was not critical to the binding/action of DIDS compared to MEF. In electrophysiological experiments with the K41C mutation, DIDS induced a leftward GV shift (~ -25 mV) whereas the normalized response was statistically non-significant. In MD simulation studies, we observed detachment of DIDS from K41C-Iks only in 3 runs out of 8 simulations. This is in contrast to Mef, where the drug left the binding site of K41C-Iks complex in all simulations.

1. Same to #2, why was the pore turret (S298-A300) not examined in Figure 7?

Again, we attempted A300C but could not get high enough expression.

Reviewer #3 (Public Review):

Weaknesses:

1. The computational aspect of the work is rather under-sampled - Figure 2 and Figure 4. The lack of quantitative analysis on the molecular dynamic simulation studies is striking, as only a video of a single representative replica is being shown per mutant/drug. Given that the simulations shown in the video are extremely short; some video only lasts up to 80 ns. Could the author provide longer simulations in each simulation condition (at least to 500 ns or until a stable binding pose is obtained in case the ligand does not leave the binding site), at least with three replicates per each condition? If not able to extend the length of the simulations due to resources issue, then further quantitative analysis should be conducted to prove that all simulations are converged and are sufficient. Please see the rest of the quantitative analysis in other comments.

We provide more quantitative analysis for the existing MD simulations and ran five additional simulations with 500 ns duration by embedding the channel in a POPC lipid membrane. For the new MD simulations, we used a different force field in order to minimize ambiguity related to force fields as well. Analysis of these data has led to new data and supplemental figures regarding RMSD of ligands during the simulations (Figure 4-figure supplement 1 and Figure 6-figure supplement 3), clustering of MD trajectories based on Mef conformation (Figure 2-figure supplement 3 and Figure 6 -figure supplement 2), H-bond formation over the simulations (Figure 2-figure supplement 4 and Figure 6-figure supplement 1). We have edited the manuscript to include this new information where appropriate.

1. Given that the protein is a tetramer, at least 12 datasets could have been curated to improve the statistic. It was also unclear how frequently the frames from the simulations were taken in order to calculate the PBSA/GBSA.

By using one ligand for each ps-IKs channel complex we tried to keep the molecular system and corresponding analysis as simple as was possible. Our initial results have shown that 4D docking and subsequent MD simulations with only one ligand bound to ps-IKs was complicated enough. Our attempts to dock 4 ligands simultaneously and analyze the properties of such a system were ineffective due to difficulties in: i) obtaining stable complexes during conformational sampling and 4D docking procedures, since the ligand interaction covers a region including three protein chains with dynamic properties, ii) possible changes of receptor conformation properties at three other subunits when one ligand is already occupying its site, iii) marked diversity of the binding poses of the ligand as cluster analysis of ligand-channels complex shows (Figure 2-figure supplement 3).

We have added a line in the methods to clarify the use of only one ligand per channel complex in simulations.

In order to calculate MMPBSA/MMGBSA we used a frame every 0.3 ns throughout the 300 ns simulation (1000 frames/simulation) or during the time the ligand remained bound. We have clarified this in the Methods.

1. The lack of labels on several structures is rather unhelpful (Figure 2B, 2C, 4B). The lack of clarity of the interaction map in Figures 2D and 6A.

We updated figures considering the reviewer's comments and added labels. For 2D interaction maps, we provided additional information in figure legends to improve clarity.

1. The RMSF analysis is rather unclear and unlabelled thoroughly. In fact, I still don't quite understand why n = 3, given that the protein is a tetramer. If only one out of four were docked and studied, this rationale needs to be explained and accounted for in the manuscript.

The rationale of conducting MD simulations with one ligand bound to IKs is explained in response to point 2 of the reviewer’s comments.

RMSF analysis in Figure 4C-E was calculated using the chain to which Mef was docked but after Mef had left the binding site. Details were added to the methods.

1. For the condition that the ligands suppose to leave the site (K42C for Mef and Y46A for DIDS), can you please provide simulations at a sufficient length of time to show that ligand left the site over three replicates? Given that the protein is a tetramer, I would be expecting three replicates of data to have four data points from each subunit. I would be expecting distance calculation or RMSD of the ligand position in the binding site to be calculated either as a time series or as a distribution plot to show the difference between each mutant in the ligand stability within the binding pocket. I would expect all the videos to be translatable to certain quantitative measures.

We have shown in the manuscript that the MEF molecule detaches from the K41C/IKs channel complex in all three simulations (at 25 ns, 70 ns and 20 ns, Table. 4). Similarly, the ligand left the site in all five new 500 ns duration simulations. We did not provide simualtions for Y46A, but Y46C left the binding site in 4 of 5 500 ns simulations and changed binding pose in the other.

Difficulties encountered upon extending the docking and MD simulations for 4 receptor sites of the channel complex is discussed in our response to point # 2 of the reviewer.

1. Given that K41 (Mef) and Y46 are very important in the coordination, could you calculate the frequency at which such residues form hydrogen bonds with the drug in the binding site? Can you also calculate the occupancy or the frequency of contact that the residues are making to the ligand (close 4-angstrom proximity etc.) and show whether those agree with the ligand interaction map obtained from ICM pro in Figure 2D?

We thank the reviewer for the suggestion to analyze the H-bond contribution to ligand dynamics in the binding site. In the plots shown in Figure 2-figure supplement 4 and Figure 6-figure supplement 1, we now provide detailed information about the dynamics of the H-bond formation between the ligand and the channel-complex throughout simulations. In addition, we have quantified this and have added these numbers to a table (Table 2) and in the text of the results.

1. Given that the author claims that both molecules share the same binding site and the mode of ligand binding seems to be very dynamic, I would expect the authors to show the distribution of the position of ligand, or space, or volume occupied by the ligand throughout multiple repeats of simulations, over sufficient sampling time that both ligand samples the same conformational space in the binding pocket. This will prove the point in the discussion - Line 463-464. "We can imagine a dynamic complex... bind/unbind from Its at a high frequency".

To support our statement regarding a dynamic complex we analyzed longer MD simulations and clustered trajectories, from this an average conformation from each cluster was extracted and provided as supplementary information which shows the different binding modes for Mef (Figure 2-figure supplement 3). DIDS was more stable in MD simulations and though there were also several clusters, they were similar enough that when using the same cut-off distance as for mefenamic acid, they could be grouped into one cluster. (Note the scale differences on dendrogram between Figure 2-figure supplement 3 and Figure 6-figure supplement 2).

1. I would expect the authors to explain the significance and the importance of the PBSA/GBSA analysis as they are not reporting the same energy in several cases, especially K41 in Figure 2 - figure supplement 2. It was also questionable that Y46, which seems to have high binding energy, show no difference in the EPhys works in figure 3. These need to be commented on.

Several studies indicate that G values calculated using MM/PBSA and MM/GBSA methods may vary. Some studies report marked differences and the reasons for such a discrepancy is thoroughly discussed in a review by Genheden and Ryde (PMID: 25835573). Therefore, we used both methods to be sure that key residues contributing to ligand binding identified with one method appear in the list of residues for which the calculations are done with the other method.

Y46C which showed only a slightly less favorable binding energy and did not unbind during 300 ns simulations, unbound, or changed pose in 4 out of 5 of the longer simulations in the presence of a lipid membrane (Figure 4-figure supplement 1). The discrepancy between electrophysiological and MD data is commented in the manuscript (pages 12-13).

1. Can the author prove that the PBSA/GBSA analysis yielded the same average free energy throughout the MD simulation? This should be the case when the simulations are converged. The author may takes the snapshots from the first ten ns, conduct the analysis and take the average, then 50, then 100, then 250 and 500 ns. The author then hopefully expects that as the simulations get longer, the system has reached equilibrium, and the free energy obtained per residue corresponds to the ensemble average.

As we mention in the manuscript, MEF- channel interactions are quite dynamic and vary even from simulation to simulation. The frequent change of the binding pose of the ligands observed during simulations (represented in Figure 2 - figure supplement 3 as clusters) is a clear reflection of such a dynamic process. Therefore, we do not expect the same average energy throughout the simulation but we do expect that G values stands above the background for key residues, which was generally the case (Figure 2 - figure supplement 2 and Figure 6.)

1. The phrase "Lowest interaction free energy for residues in ps-KCNE1 and selected KCNQ1 domains are shown as enlarged panels (n=3 for each point)" needs further explanation. Is this from different frames? I would rather see this PBSA and GBSA calculated on every frame of the simulations, maybe at the one ns increment across 500 ns simulations, in 4 binding sites, in 3 replicas, and these are being plotted as the distribution instead of plotting the smallest number. Can you show each data point corresponding to n = 3?

The MMPBSA/MMGBSA was calculated for 1000 frames across 3x300 ns simulations with 0.3 ns sampling interval, together 3000 frames, shown in Figure 2-figure supplement 2 and includes error bars to show the differences across runs. We have updated the legend for greater clarity.

1. I cannot wrap my head around what you are trying to show in Figure 2B. This could be genuinely improved with better labelling. Can you explain whether this predicted binding pose for Mef in the figure is taken from the docking or from the last frame of the simulation? Given that the binding mode seems to be quite dynamic, a single snapshot might not be very helpful. I suggest a figure describing different modes of binding. Figure 2B should be combined with figure 2C as both are not very informative.

We have updated Figure 2B with better labelling and added a new figure showing the different modes of binding (Figure 2-figure supplement 3).

1. Similar to the comment above, but for Figure 4B. I do not understand the argument. If the author is trying to say that the pocket is closed after Mef is removed - then can you show, using MD simulation, that the pocket is openable in an apo to the state where Mef can bind? I am aware that the open pocket is generated through batches of structures through conformational sampling - but as the region is supposed to be disordered, can you show that there is a possibility of the allosteric or cryptic pocket being opened in the simulations? If not, can you show that the structure with the open pocket, when the ligand is removed, is capable of collapsing down to the structure similar to the cryo-EM structure? If none of the above work, the author might consider using PocketMiner tools to find an allosteric pocket (https://doi.org/10.1038/s41467-023-36699-3) and see a possibility that the pocket exists.

Please see the attached screenshot which depicts the binding pocket from the longest run we performed (1250 ns) before drug detachment (grey superimposed structures) and after (red superimposed structures). Mefenamic acid is represented as licorice and colored green. Snapshots for superimposition were collected every 10 ns. As can be seen in the figure, when the drug leaves the binding site (after 500 ns, structures colored red), the N-terminal residue of psKCNE1, W323, and other residues that form the pocket shift toward the binding site, overlapping with where Mefenamic acid once resided. The surface structure in Figure 4B shows this collapse.

Author response image 1.

In the manuscript, we propose that drug binding occurs by the mechanism that could be best described by induced fit models, which state that the formation of the firm complexes (channel-Mef complex) is a result of multiple-states conformational adjustments of the bimolecular interaction. These interactions do not necessarily need to have large interfaces at the initial phase. This seems to be the case in Mef with IKS interactions, since we could not identify a pocket of appropriate size either using PocketMiner software suggested by the reviewer or with PocketFinder tool of ICM-pro software.

1. Figure 4C - again, can you show the RMSF analysis of all four subunits leading to 12 data points? If it is too messy to plot, can you plot a mean with a standard deviation? I would say that a 1-1.5 angstroms increase in the RMSF is not a "markedly increased", as stated on line 280. I would also encourage the authors to label whether the RMSF is calculated from the backbone, side-chain or C-alpha atoms and, ideally, compare them to see where the dynamical properties are coming from.

Please see the answer to comment #4. We agree that the changes are not so dramatic and modified the text accordingly. RMSD was calculated for backbone atom to compare residues with different side chains, a note of this is now in the methods and statistical significance of ps-IKs vs K41C, W323A and Y46C is indicated in Figures 4C-4E.

1. In the discussion - Lines 464-467. "Slowed deactivation of the S1/KCNE1/Pore domain/drug complex... By stabilising the activated complex. MD simulation suggests the latter is most likely the case." Can you point out explicitly where this has been proven? If the drug really stabilised the activated complex, can you show which intermolecular interaction within E1/S1/Pore has the drug broken and re-form to strengthen the complex formation? The authors have not disproven the point on steric hindrance either. Can this be disproved by further quantitative analysis of existing unbiased equilibrium simulations?

The stabilization of S1/KCNE1/Pore by drugs does not necessarily have to involve a creation of new contacts between protein parts or breakage of interfaces between them. The stabilization of activated complexes by drugs may occur when the drug simultaneously binds to both moveable parts of the channel, such as voltage sensor(s) or upper KCNE1 region, and static region(s) of the channel, such as the pore domain. We have changed the corresponding text for better clarity.

1. Figure 4D - Can you show this RMSF analysis for all mutants you conducted in this study, such as Y46C? Can you explain the difference in F dynamics in the KCNE3 for both Figure 4C and 4D?

We now show the RMSF for K41C, W323A and Y46C in Figure 4C-E. We speculate that K41 (magenta) and W323 (yellow), given their location at the lipid interface (see Author response image 1), may be important stabilizing residues for the KCNE N-terminus, whereas Y46 (green) which is further down the TMD has less of an impact.

Author response image 2.

1. Line 477: the author suggested that K41 and Mef may stabilise the protein-protein interface at the external region of the channel complex. Can you prove that through the change in protein-protein interaction, contact is made over time on the existing MD trajectories, whether they are broken or formed? The interface from which residues help to form and stabilise the contact? If this is just a hypothesis for future study, then this has to be stated clearly.

It is known that crosslinking of several residues of external E1 with the external pore residues dramatically stabilizes voltage-sensors of KCNQ1/KCNE1 complex in the up-state conformation. This prevents movable protein regions in the voltage-sensors returning to their initial positions upon depolarization, locking the channel in an open state. We suggest that MEF may restrain the backward movement of voltage-sensors in a similar way that stabilizes open conformation of the channel. The stabilization of the voltage sensor domain through MEF occurs due to contacts of the drug with both static (pore domain) and dynamic protein parts (voltage-sensors and external KCNE1 regions). We have changed the corresponding part of the text.

1. The author stated on lines 305-307 that "DIDS is stabilised by its hydrophobic and vdW contacts with KCNQ1 and KCNE1 subunits as well as by two hydrogen bonds formed between the drug and ps-KCNE1 residue L42 and KCNQ1 residue Q147" Can you show, using H-bond analysis that these two hydrogen bonds really exist stably in the simulations? Can you show, using minimum distance analysis, that L42 are in the vdW radii stably and are making close contact throughout the simulations?

We performed a detailed H-bond analysis (Figure 6-supplement figure 1) which shows that DIDS forms multiple H-bond over the simulations, though only some of them (GLU43, TYR46, ILE47, SER298, TYR299, TRP323 ) are stable. Thus, the H-bonds that we observed in DIDS-docking experiments were unstable in MD simulations. As in the case of the IKs-MEF complex, the prevailing H-bonds exhibit marked quantitative variability from simulation to simulation. We have added a table detailing the most frequent H-bonds during MD simulations (Table 2).

1. Discussion - In line 417, the author stated that the "S1 appears to pull away from the pore" and supplemented the claim with the movie. This is insufficient. The author should demonstrate distance calculation between the S1 helix and the pore, in WT and mutants, with and without the drug. This could be shown as a time series or distribution of centre-of-mass distance over time.

We tried to analyze the distance changes between the upper S1 and the pore domain but failed to see a strong correlation We have removed this statement from the discussion.

1. Given that all the work were done in the open state channel with PIP2 bound (PDB entry: 6v01), could the author demonstrate, either using docking, or simulations, or alignment, or space-filling models - that the ligand, both DIDS and Mef, would not be able to fit in the binding site of a closed state channel (PDB entry: 6v00). This would help illustrate the point denoted Lines 464-467. "Slowed deactivation of the S1/KCNE1/Pore domain/drug complex... By stabilising the activated complex. MD simulation suggests the latter is most likely the case."

As of now, a structure representing the closed state of the channel does not exist. 6V00 is the closed inactivated state of the channel pore with voltage-sensors in the activated conformation. In order to create simulation conditions that reliably describe the electrophysiological experiments, at least a good model for closed channels with resting state voltage sensors is necessary.

1. The author stated that the binding pose changed in one run (lines 317 to 318). Can you comment on those changes? If the pose has changed - what has it changed to? Can you run longer simulations to see if it can reverse back to the initial confirmation? Or will it leave the site completely?

Longer simulations and trajectory clustering revealed several binding modes, where one pose dominated in approximately 50% of all simulations in Figure 2-figure supplement 3 encircled with a blue frame.

1. Binding free energy of -32 kcal/mol = -134 kJ/mol. If you try to do dG = -RTlnKd, your lnKd is -52. Your Kd is e^-52, which means it will never unbind if it exists. I am aware that this is the caveat with the methodologies. But maybe these should be highlighted throughout the manuscript.

We thank the reviewer for this comment. G values, and corresponding Kd values, calculated from simulation of Mef-ps-IKs complex do not reflect the apparent Kd values determined in electrophysiological experiments, nor do they reflect Kd values of drug binding that could be determined in biochemical essays. Important measures are the changes observed in simulations of mutant channel complexes relative to wild type. We now briefly mention this issue in the manuscript.

Reviewer #1 (Recommendations For The Authors):

1) It would be nice to have labels of amino acid residues in Figure 2B.

We updated Figure 2B and added some residue labels.

2) Fig. 3A and 7A. In what order the current traces are presented? I don't see the rule.

We have now arranged the current traces in a more orderly manner, listing them first by ascending KCNE1 residue numbers and then by ascending KCNQ1 residue numbers. Now consistent with Fig 3 and 7 (normalized response and delta V1/2).

3) Line 312 "A44 and Y46 were more so." A44 may be more critical, but I can't see Y46 is more, according to Figure 2-figure supplement2 and Figure 6.

Indeed, comparison of the energy decomposition data indicates approximately the same ∆G values for Y46. We have revised this in the text correspondingly.

4) Line 267 "Mefenamic acid..." I would like to see the movie.

We no longer have access to this original movie

5) In supplemental movies 5-7, the side chains of some critical amino acid residues (W323, K41) would be better presented as in movies 1-4.

We have retained the original presentations of these movies as the original files are no longer available.

Reviewer #2 (Recommendations For The Authors):

General comments:

1) To determine the effect of mefenamic acid and DIDS on channel closing kinetics, a protocol in which they step from an activating test pulse to a repolarizing tail pulse to -40 mV for 1 s is used. If I understand it right, the drug response is assessed as the difference in instantaneous tail current amplitude and the amplitude after 1 s (row 599-603). The drug response of each mutant is then normalized to the response of the WT channel. However, for several mutants there is barely any sign of current decay during this relatively brief pulse (1 s) at this specific voltage. To determine drug effects more reliably on channel closing kinetics/the extent of channel closing, I wonder if these protocols could be refined? For instance, to cover a larger set of voltages and consider longer timescales?

To clarify, the drug response of each mutant is not normalized to the response of the WT channel. In fact, our analysis is not meant to compare mutant and WT tail current decay but rather how isochronal tail current decay is changed in response to drug treatment in each channel construct. As acknowledged by the reviewer, the peak to end difference currents were calculated by subtracting the minimum amplitude of the deactivating current from the peak amplitude of the deactivating current. But the difference current in mefenamic acid or DIDS was normalized to the maximum control (in the absence of drug) difference current and subtracted from 1.0 to obtain the normalized response. Thus, the difference in tail current decay in the absence and in the presence of drug is measured within the same time scale and allow a direct comparison between before and after drug treatment. As shown in Fig 3D and 7C, a large drug response such as the one measured in WT channels is reflected by a value close to 1. A smaller drug response is indicated by low values. We recognize that some mutations resulted in an intrinsic inhibition of tail current decay in the absence of drug, which potentially lead to underestimating the normalized response value. Our goal was not to study in detail the effects of the drug on channel closing kinetics, but only to determine the impact of the mutation on drug binding by using tail current decay as a readout. Consequently, we believe that the duration of the deactivating tail current used in this experiment was sufficient to detect drug-induced tail current decay inhibition.

2) The effect of mefenamic acid seems to be highly dependent on the pulse-to-pulse interval in the experiments. For instance, for WT in Figure 3 - Figure supplement 1, a 15 s pulse-to-pulse interval provides a -100 mV shift in V1/2 induced by mefenamic acid, whereas there is no shift induced when using a 30 s pulse-to-pulse interval. Can the authors explain why they generally consider a 15 s pulse-to-pulse interval more suitable (physiologically relevant?) in their experiments to assess drug effects?

In our previous experiments, we have determined that a 15 s inter-pulse interval is generally adequate for the WT IKs channels to fully deactivate before the onset of the next pulse. Consistent with our previous work (Wang et al. 2019), we observed that in wild-type EQ channels, there is no current summation from one pulse to the next one (see Fig 1A, bottom panel). This is important as the IKs channel complex is known to be frequency dependent i.e. current amplitude increases as the inter-pulse interval gets shorter. Such current summation results in a leftward shift of the conductance-voltage (GV) relationship. This is also important with regards to drug effects. As indicated by the reviewer, mefenamic acid effects are prominent with a 15 sec inter-pulse interval but less so with a 30 sec inter-pulse interval when enough time is given for channels to more completely deactivate. Full effects of mefenamic acid would have therefore been concealed with a 30sec inter-pulse interval.

Moreover, our patch-clamp recordings aim to explore the distinct responses of mutant channels to mefenamic acid and DIDS in comparison to the wild-type channel. It is important to note that the inter-pulse interval's physiological relevance is not necessarily crucial in this context.

3) Related to comment 1 and 2, there is a large diversity in the intrinsic properties of tested mutants. For instance, V1/2 ranges from 4 to 70 mV. Also, there is large variability in the slope of the G-V curves. Whether channel closing kinetics, or the impact of pulse-to-pulse interval, vary among mutants is not clear. Could the authors please discuss whether the intrinsic properties of mutants may affect their ability to respond to mefenamic acid and DIDS? Also, please provide representative current families and G-V curves for all assessed mutants in supplementary figures.

The intrinsic properties of some mutants vary from the WT channels and influence their responsiveness to mefenamic acid and DIDS. The impact of the mutations on the IKs channel complex are reflected by changes in V1/2 (Table 1, 4) and tail current decay (Figs. 3, 7). But, it is the examination of the drug effects on these intrinsic properties (i.e. GV curve and tail current decay) that constitutes the primary endpoint of our study. We consider that the degree by which mef and DIDS modify these intrinsic properties reflects their ability to bind or not to the mutated channel. In our analysis, we compared each mutant's response to mefenamic acid and DIDS with its respective control. Consequently, the intrinsic properties of the mutant channels have already been considered in our evaluation. As requested, we have provided representative current families and G-V curves for all assessed mutants in Figure 3-figure supplement 1 and Figure 7-figure supplement 1.

4) The A44C and Y148C mutants give strikingly different currents in the examples shown in Figure 3 and Figure 7. What is the reason for this? In the examples in figure 7, it almost looks like KCNE1 is absent. Although linked constructs are used, is there any indication that KCNE1 is not co-assembled properly with KCNQ1 in those examples?

The size of the current is critical to determining its shape, as during the test pulse there is some endogenous current mixed in which impacts shape. A44C and Y148C currents shown in Figure 7 are smaller with a larger contribution of the endogenous current, mostly at the foot of the current trace. In our experience there is little endogenous current in the tail current at -40 mV and for this reason we focus our measurements there.

Although constructs with tethered KCNQ1 and KCNE1 were used, we cannot rule out the possibility that Q1 and E1 interaction was altered by some of the mutations. Several KCNE1 and KCNQ1 residues have been identified as points of contact between the two subunits. For instance, the KCNE1 loop (position 36-47) has been shown to interact with the KCNQ1 S1-S2 linker (position 140-148) (Wang et al, 2011). Thus, it is conceivable that mutation of one or several of those residues may alter KCNQ1/KCNE1 interaction and modify the activation/deactivation kinetics of the IKs channel complex.

5) I had a hard time following the details of the simulation approaches used. If not already stated (I could not find it), please provide: i) details on whether the whole channel protein was considered for 4D docking or a docking box was specified, ii) information on how simulations with mutant ps-IKs were prepared (for instance with the K41C mutant), especially whether the in silico mutated channel was allowed to relax before evaluation (and for how long). Also, please make sure that information on simulation time and number of repeats are provided in the Methods section.

For 4D docking, only residues within 0.8 nm of psKCNE1 residues D39-A44 were selected. Complexes with mutated residues were relaxed using the same protocol as the WT channel, (equilibration with gradually releasing restraints with a final equilibration for 10 ns where only the backbone was constrained with 50 kcal/mol/nm2). We have updated the methods accordingly.

Specific comments:

In figure legends, please provide information on whether data represents mean +/- SD or SEM. Also, please provide information on which statistical test was used in each figure.

We revised the figure legend to add the nature of the statistical test used.

G-V curves are normalized between 0 and 1. However, for many mutants the G-V relationship does not reach saturation at depolarized voltages. Does this affect the estimated V1/2? I could not really tell as I was not sure how V1/2 was determined for different mutants (could the explanation on row 595-598 be clarified)?

The primary focus here is in the shift between the control response and drug response for each mutant, rather than the absolute V1/2 values. The isochronal G-V curves that are generated for each construct (WT and mutant) utilize an identical voltage protocol. This approach ensures a uniform comparison among all mutants. By observing the shifts in these curves, we can gain insight into the response of mutant channels to the drug. This information ultimately helps elucidate the inherent properties of the mutant channels and contributes to our understanding of the drug's binding mechanism to the channel.

As requested by the reviewer, we also clarified the way V1/2 was generated: When the G-V curve did not reach zero, the V1/2 value was directly read from the plot at the voltage point where the curve crossed the 0.5 value on the y coordinate.

A general comment is that the Discussion is fairly long and some sections are quite redundant to the Results section. The authors could consider focusing the text in the Discussion.

We changed the discussion correspondingly wherever it was appropriate.

I found it a bit hard to follow the authors interpretation on whether their drug molecules remain bound throughout the experiments, or whether there is fast binding/unbinding. Please clarify if possible.

In the 300 ns MD simulations mefenamic acid and DIDS remained stably bound to WT-ps-IKS, binding of drugs to mutant complexes are described in the Table 3 and Table 5. In longer simulations with the channel embedded in a lipid environment, mefenamic acid unbinds in two out of five runs for WT-ps-IKs (Figure 4 – figure supplement 1), and DIDS shows a few events where it briefly unbinds (Figure 6 -figure supplement 3). Based on electrophysiological data we speculate that drugs might bind and unbind to WT-ps-IKs during the gating process. We do not see bind-unbinding in MD simulations, since the model we used in simulations reflects only open conformation of the channel-complex with an activated-state voltage-sensor, whereas a resting-state voltage sensor condition was not considered.

The authors have previously shown that channels with no, one or two KCNE1 subunits are not, or only to a small extent, affected by mefenamic acid (Wang et al., 2020). Could the details of the binding site and proposed mechanisms of action provide clues as to why all binding sites need to be occupied to give prominent drug effects?

In the manuscript, we propose that the binding of drugs induces conformational changes in the pocket region that stabilize S1/KCNE1/Pore complex. In the tetrameric channel with 4:4 alpha to beta stoichiometry the drugs are likely to occupy all four sites with complete stabilization of S1/KCNE1/Pore. When one or more KCNE1 subunits is absent, as in case of EQQ, or EQQQQ constructs, drugs will bind to the site(s) where KCNE1 is available. This will lead to stabilization of the only certain part of the S1/KCNE1/Pore complex. We believe that the corresponding effect of the drug, in this case will be partially effective.

There is a bit of jumping in the order of when some figures are introduced (e.g. row 178 and 239). The authors could consider changing the order to make the figures easier to follow.

We have changed the corresponding section appropriately to improve the reading flow.

Row 237: "Data not shown", please show data.

The G-V curve of the KCNE1 Y46C mutant displays a complex, double Boltzmann relationship which does not allow for the calculation of a meaningful V1/2 nor would it allow for an accurate determination of drug effects. Consequently, we have excluded it from the manuscript.

In the Discussion, the author use the term "KCNE1/3". Does this correspond to the previous mention of "ps-KCNE1"?

Yes, this refers to ps-KCNE1. We have changed it correspondingly.

Row 576: When was HMR 1556 used?

While HMR 1556 was used in preliminary experiments to confirm that the recorded current was indeed IKs, it does not provide substantial value to the data presented in our study or our experiments. As a result, we have excluded HMR 1556 experiments from the final results and have revised the Methods section accordingly.

Reviewer #3 (Recommendations For The Authors):

1) Figures 2D and 6A are very unclear. Can the authors provide labels as text rather than coloured circles, whether the residue is on Q1 or E1? There is also a distance label in the figure in the small font with the faintest shade of grey, which I believe is supposed to be hydrogen bonds. Can this be improved for clarity?

We feel that additional labels on the ligand diagrams to be more confusing, instead, we updated the description in the legend and added labels to Figure 2B and Figure 6B to improve the clarity of residue positions. In addition, we have added 2 new figures with more detailed information about H-bonds (Figure 2-figure supplement 4, Figure 6- figure supplement 1).

2) Figure 2B - all side chains need labelling in different binding modes. The green ligand on blue protein is very difficult to see. Suddenly, the ligand turns light blue in panel 2C. Can this be consistent throughout the manuscript?

Figure 2B is updated according to this comment.

3) Figure 2 - figure supplement 2, and figure 6B. Can the author show the residue number on the x-axis instead of just the one-letter abbreviation? This requires the reader to count and is not helpful when we try to figure out where the residue is at a glance. I would suggest a structure label adjacent to the plot to show whether they are located with respect to the drug molecule.

Since the numbers for residues on either end of the cluster are indicated at the bottom of each boxed section, we feel that adding residue numbers would just further clutter the figure.

4) Figure 2 - figure supplement 2, and Figure 6B. Can you explain what is being shown in the error bar? I assume standard deviation?

Error bars on Figure 2-figure supplement 2 represent SEM. We added corresponding text in the figure legend.

5) Figure 2 - figure supplement 2, and figure 6B. Can you explain how many frames are being accounted for in this PBSA calculation?

For Figure 2- figure supplement 2 and Figure 6B a frame was made every 0.3 ns over 3x300 ns simulation, 1000 frames for each simulation, 3000 frames overall.

6) Figure 3D/E and 7C/D, it would be helpful to show which mutant show agreeable results with the simulations, PBSA/GBSA and contact analyses as suggested above.

The inconsistencies and discrepancies between the results of MD simulations and electrophysiological experiments are discussed throughout the manuscript.

7) Figure legend, figure 3E - I assume that there is a type that is different mutants with respect to those without the drug. Otherwise, how could WT, with respect to WT, has -105 mV dV1/2?

The reviewer is correct in that the bars indicate the difference in V1/2 between control and drug treatment. Thus, the difference in V1/2 (∆V1/2) between the V1/2 calculated for WT control and the V1/2 for mefenamic acid is indeed -105 mV. We have now revised Figure 3E's legend to accurately reflect this and ensure a clear understanding of the data presented.

8) Figure 3 - figure supplement 1B is very messy, and I could not extract the key point from it. Can this be plotted on a separate trace? At least 1 WT trace and one mutant trace, 1 with WT+drug and one mut+drug as four separate plots for clarity?

The key message of this figure is to illustrate the similarities of EQ WT + Mef and EQ L142C data. Thus, after thorough consideration, we have concluded that maintaining the current figure, which displays the progressive G-V curve shift in EQ WT and L142C in a superimposed manner, best illustrates the gradual shift in the G-V curves. This presentation allows for a clearer and more immediate comparison of the curve shifts, which may be more challenging to discern if the G-V curves were separated into individual figures. We believe that the existing format effectively communicates the relevant information in a comprehensive and accessible manner.

9) Figure 4B - the label Voltage is blended into the orange helix. Can the label be placed more neatly?

We altered the labels for this figure and added that information in the figure description.

10) Can you show the numerical label of the residue, at least only to the KCNE1 portion in Figures 4C and 4D?

We updated these figures and added residue numbering for clarity.

11) Can you hide all non-polar hydrogen atoms in figure 8 and colour each subunit so that it agrees with the rest of the manuscripts? Can you adjust the position of the side chain so that it is interpretable? Can you summarise this as a cartoon? For example, Q147 and Y148 are in grey and are very far hidden away. So as S298. Can you colour-code your label? The methionine (I assume M45) next to T327 is shown as the stick and is unlabelled. Maybe set the orthoscopic view, increase the lighting and rotate the figures in a more interpretable fashion?

We agree that Fig.8 is rather small as originally presented. We have tried to emphasize those residues we feel most critical to the study and inevitably that leads to de-emphasis of other, less important residues. As long as the figure is reproduced at sufficient size we feel that it has sufficient clarity for the purposes of the Discussion.

12) Line 538-539. Can you provide more detail on how the extracellular residues of KCNE3 are substituted? Did you use Modeller, SwissModel, or AlphaFold to substitute this region of the KCNEs?

We used ICM-pro to substitute extracellular residues of KCNE3 and create mutant variants of the Iks channel. This information is provided in the methods section now.

13) Line 551: The PIP2 density was solved using cryo-EM, not X-ray crystallography.

We corrected this.

14) Line 555: The system was equilibrated for ten ns. In which ensemble? Was there any restraint applied during the equilibration run? If yes, at what force constant?

The system was equilibrated in NVT and NPT ensembles with restraints. These details are added to methods. In the new simulations, we did equilibrations gradually releasing spatial from the backbone, sidechains, lipids, and ligands. A final 30 ns equilibration in the NPT ensemble was performed with restraint only for backbone atoms with a force constant of 50 kJ/mol/nm2. Methods were edited accordingly.

15) Line 557: Kelvin is a unit without a degree.

Corrected

16) Line 559: PME is an electrostatic algorithm, not a method.

Corrected

17) Line 566: Collecting 1000 snapshots at which intervals. Given your run are not equal in length, how can you ensure that these are representative snapshots?

Please see comment #5.

18) Table 3 - Why SD for computational data and SEM for experimental data?

There was no particular reason for using SD in some graphs. We used appropriate statistical tests to compare the groups where the difference was not obvious.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Using lineage tracing and single-cell RNA sequencing, Li et al. reported brain ECs can differentiate into pericytes after stroke. This finding is novel and important to the field.

Strengths:

Detailed characterization of each time point and genetic manipulation of genes for study role of ECs and E-pericyte.

Weaknesses:

Genetic evidence for lineage tracing of ECs and E-pericytes requires more convincing data that includes staining, FACS, and scRNA-seq analysis.

We appreciate the reviewer’s recommendation to explore more convincing data, including staining, FACS, and scRNA-seq analysis. We initially employed traditional lineage tracing methods to demonstrate that endothelial cells can transform into pericytes after stroke. We utilized Cdh5CreERT2;Ai47 mice, Tie2-Dre;Mfsd2aCreER;Ai47 mice, and AAV-BI30 virus-infected Ai47 mice. However, in our validation of the transformed cells as pericytes, there are limitations to our results. While three pericyte markers (CD13, NG2, and PDGFRβ) were used in Cdh5CreERT2;Ai47 mice, only one marker (CD13) was applied in Tie2Dre; Mfsd2aCreER;Ai47 and AAV-BI30 virus-infected Ai47 mice. This is insufficient, and the other two pericyte markers (NG2 and PDGFRβ) need to be verified in these models.

At scRNA-seq, although we observed an increased proportion of pericyte/EGFP⁺ cells after stroke, we did not rule out potential contamination by pericyte cells, nor did we include sufficient replicates. To address these issues, we can explore additional methods for analyzing scRNA-seq data, increasing sample replicates, and eliminating pericyte contamination using advanced algorithms. Furthermore, we can use chimeric-related mutations to compare normal endothelial cells, normal pericytes, endothelial-derived pericytes (E-pericytes), and intermediate fibroblast-like cells at the DNA level. This approach will help identify and trace chimeric-related mutations across different cell types and developmental stages. Finally, we can track the entire process of endothelial cell transformation into pericytes using two-photon imaging in vivo.

Reviewer #2 (Public review):

Summary:

In this manuscript, Li and colleagues study the fate of endothelial cells in a mouse model of ischemic stroke. Using genetic lineage tracing approaches, they found that endothelial cells give rise to non-endothelial cells, which they term "E-pericytes." They further show that depleting these cells exacerbates blood-brain barrier leakage and worsens functional recovery. The authors also provide evidence that endothelial-to-mesenchymal transition, myeloid cell-derived TGFβ1, and endothelial TGFβRII are involved in this process. These are potentially interesting findings, however, the experimental evidence that endothelial cells undergo transdifferentiation to non-endothelial cells is weak, as is the evidence that these cells are pericytes. Addressing this foundational weakness will facilitate the interpretation of the other findings.

Strengths:

(1) The authors address an important question about blood vessel function and plasticity in the context of stroke.

(2) The authors use a variety of genetic approaches to understand cell fate in the context of stroke. Particularly commendable is the use of several complementary lineage tracing strategies, including an intersectional strategy requiring both endothelial Cre activity and subsequent mural cell NG2 promoter activity.

(3) The authors address upstream cellular and molecular mechanisms, including roles for myeloid-derived TGFβ.

Weaknesses:

(1) The authors use Cdh5-CreERT2; Ai47 mice to permanently label endothelial cells and their progeny with eGFP. They then isolate eGFP⁺ cells from control and MCAO RP7D and RP34D brains, and use single-cell RNA-seq to identify the resulting cell types. Theoretically, all eGFP⁺ cells should be endothelial cells or their progeny. This is a very powerful and well-conceived experiment. The authors use the presence of a pericyte cluster as evidence that endothelial-to-pericyte transdifferentiation occurs. However, pericytes are also present in the scRNA-seq data from sham mice, as are several other cell types such as fibroblasts and microglia. This suggests that pericytes and these other cell types might have been co-purified (e.g., as doublets) with eGFP⁺ endothelial cells during FACS and may not themselves be eGFP⁺. Pericyte-endothelial doublets are common in scRNA-seq given that these cell types are closely and tightly associated. Additionally, tight association (e.g., via peg-socket junctions) can cause fragments of endothelial cells to be retained on pericytes (and vice-versa) during dissociation. Finally, it is possible that after stroke or during the dissociation process, endothelial cells lyse and release eGFP that could be taken up by other cell types. All of these scenarios could lead to the purification of cells that were not derived (transdifferentiated) from endothelial cells. The authors note that the proportion of pericytes increased in the stroke groups, but it does not appear this experiment was replicated and thus this conclusion is not supported by statistical analysis. The results of pseudotime and trajectory analyses rely on the foundation that the pericytes in this dataset are endothelial-derived, which, as discussed above, has not been rigorously demonstrated.

Thank you for your thoughtful comment.

Indeed, we face the challenge of obtaining pure cells. As the reviewer has pointed out, several factors may contribute to cell contamination. For instance, the meninges of adult mice are difficult to remove completely, which may lead to fibroblast contamination. Although Cdh5CreERT2 can specifically label endothelial cells in the normal brain parenchyma, there may still be very few unspecific cells in certain brain regions, such as the choroid plexus and periventricular areas, resulting in the presence of ependymal cells. To address these issues, we can improve our methodology by carefully removing the meninges, choroid plexus, and periventricular cells during sample preparation. Additionally, we need to increase the N of the transcriptome samples to enhance the reliability of our data.

(2) I have the same concern regarding the inadvertent purification of cells that were not derived from endothelial cells in the context of the bulk RNA-seq experiment (Figure S4), especially given the sample-to-sample variability in gene expression in the RP34D, eGFP⁺ non-ECs-group (e.g., only 2/5 samples are enriched for mesenchymal transcription factor Tbx18, only 1/5 samples are enriched for mural cell TF Heyl). If the sorted eGFP⁺ non-ECs were pericytes, I would expect a strong and consistent pericyte-like gene expression profile.

This is an interesting question.

Indeed, significant differences were observed in the expression of pericyte-related transcriptional profiles within the eGFP⁺ non-ECs group. For instance, transcription factors such as Hic1 and Fosl1 were nearly absent in the eGFP⁺ non-ECs group. We propose several potential explanations for these observations:

(1) The sorted eGFP⁺ non-ECs group may contain other cell types, leading to contamination.

(2) The eGFP⁺ non-ECs group may not uniformly express all pericyte-related transcriptional profiles.

(3) The temporal dynamics of transcription factor expression (i.e., different factors being expressed at different stages) could contribute to the observed variability.

(4) The heterogeneity in the timing of endothelial-to-pericyte transformation (i.e., some cells have already transformed into pericytes while others are in the process of transformation at the early stage) may result in significant differences in transcriptional profiles.

(3) The authors use immunohistochemistry to understand localization, morphology, and marker expression of eGFP⁺ cells in situ. The representative "E-pericytes" shown in Figure 3A-D are not associated with blood vessels, and the authors' quantification also shows that the majority of such cells are not vessel-associated ("avascular"). By definition, pericytes are a component of blood vessels and are embedded within the vascular basement membrane. Thus, concluding that these cells are pericytes ("E-pericytes") may be erroneous.

Yes, we found that 72.2% of E-pericytes were free and not associated with blood vessels. Normally, pericytes surround blood vessels and connect to endothelial cells. However, in certain diseases, such as Alzheimer's disease, stroke, and diabetic encephalopathy, pericytes can detach from blood vessels. In our stroke model, we observed that pericytes detach from blood vessels. This phenomenon can be explained by two possible scenarios:

(1) After endothelial cells transform into E-pericytes, the E-pericytes detach from blood vessels due to the pathological environment following stroke.

(2) After stroke, blood vessel function is impaired, leading to vascular degeneration. Endothelial cells shed from the blood vessels and subsequently transform into E-pericytes.

Therefore, preventing pericyte detachment from blood vessels after stroke represents an important scientific challenge.

(4) CD13 flow cytometry and immunohistochemistry are used extensively to identify pericytes. In the context of several complementary lineage tracing strategies noted in Strength #2, CD13 immunohistochemistry is the only marker used to identify putative pericytes (Figure S3J-M). In stroke, CD13 is not specific to pericytes; dendritic cells and other monocyte-derived cells express CD13 (Anpep) in mouse brain after stroke (PMID: 38177281, https://anratherlab.shinyapps.io/strokevis/).

We thank the reviewer for their valuable input. In the context of stroke, CD13 is not specific to pericytes. Additionally, pericytes lack a single specific marker; instead, their identity is determined by a combination of multiple markers. To more convincingly validate the identity of pericytes, it is necessary to incorporate additional pericyte markers alongside several complementary lineage tracing strategies.

(5) The authors conclude that "EC-specific overexpression of the Tgfbr2 protein by a virus (Tgfbr2) decreases Evans blue leakage, promotes CBF recovery, alleviates neurological deficits and facilitates spontaneous behavioral recovery after stroke by increasing the number of E-pericytes." All data in Figure 10, however, compare endothelial Tgfbr2 overexpression to a DsRed overexpression control. There is no group in which Tgfbr2 is overexpressed but "E-pericytes" are eliminated with DTA (this is done in Figure 9B, but this experiment lacks the Tgfbr2 overexpression-only control). Thus, the observed functional outcomes cannot be ascribed to "E-pericytes"; it remains possible that endothelial Tgfbr2 overexpression affects EB leakage, CBF, and behavior through alternative mechanisms.

We thank the reviewer for their valuable comment. Although in Figures 9A-B, we observed no significant difference in Evans blue leakage between the Tgfbr2 overexpression group and the Tgfbr2 overexpression + DTA group (P=0.8153), this suggests that the impact of Tgfbr2 overexpression on the blood-brain barrier (BBB) is primarily attributed from the E-pericytes generated by Tgfbr2 expression. Furthermore, in Figure 10A, the inclusion of the Tgfbr2 overexpression + DTA group would provide stronger evidence that the effects of Tgfbr2 overexpression on the BBB and neurobehavioral outcomes are mainly due to the E-pericytes derived from Tgfbr2 expression.

(6) Single-cell and bulk RNA-seq data are not available in a public repository (such as GEO). Depositing these data would facilitate their independent reevaluation and reuse.

Thank you for the suggestion and we have uploaded Single-cell and bulk RNA-seq data (The assignment of GEO number is pending).

Reviewer #3 (Public review):

Summary:

The data and experiments presented in that study convincingly show that a subpopulation of endothelial cells undergo transformation into pericyte-like cells after stroke in mice. These so-called "E-pericytes" are protective and might present a new target for stroke recovery. The authors used a huge battery of different techniques and modified signaling pathways and cellular interactions using several genetic and pharmacological tools to show that TGFbeta and EndoMT are causes of this transformation.

Strengths:

The amount of different genetic and pharmacological approaches in combination with sophisticated techniques such as single-cell RNAseq is impressive and convincing. The results support their conclusions and the authors achieved their aims. The findings will strongly impact the field of cerebrovascular recovery after stroke and might open up new therapeutic targets.

Weaknesses:

The written and graphic presentation of the findings needs substantial improvement. Language editing is strongly recommended (there are a lot of spelling and grammatical errors in the text and illustrations, including legends).

Thank you for raising this important point and we will place greater emphasis on the written and graphic presentation of the findings.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

In this study, Li et al. reported that endothelial cells in the brain can differentiate into pericytes to promote the restoration of blood-brain barrier (BBB) function after stroke. Understanding the mechanisms underlying BBB restoration post-stroke is crucial to the field. Using lineage tracing, RNA sequencing (RNA-seq), and immunostaining, Li et al. detected the transdifferentiation of endothelial cells (ECs) into E-pericytes in the middle cerebral artery occlusion (MCAO) model. The specific knockout of Tgfbr2 in ECs reduced the number of E-pericytes, exacerbated BBB leakage, and worsened neurological deficits. This observation of EC to pericyte differentiation is novel; however, the conclusions at this stage are not fully supported by the evidence provided.

(1) The authors claimed, based on the EdU assay, that 12.9% of pericytes present at RP34D originated from self-proliferation, while the origin of the remaining 27.6% of new pericytes remains unclear. This raises concerns, as the EdU assay is not 100% efficient in detecting all proliferating cells. If EdU⁺ ECs account for fewer than 10% of all ECs, it follows that other EdU-ECs must have alternative origins.

That is an interesting question. To address this issue, we need to consider the following aspects:

(1) The EdU assay is not 100% efficient in detecting all proliferating cells, which means that the actual proportion of proliferating pericytes may be higher than 12.9%, while the proportion of pericytes from other sources may be lower than 27.6% (as determined by FACS). This is consistent with the observation in Figure 3H (immunofluorescence analysis), where EGFP⁺ pericytes accounted for only 24.5% of all pericytes.

(2) The dose of EdU administered in our study was relatively high (200 mg/kg, intraperitoneal injection, daily), which may increase the efficiency of EdU labeling.

(3) When EdU⁺ endothelial cells (ECs) constitute less than 10% of all ECs, it does suggest that EdU-ECs could be a source of pericytes. However, at least EdU⁺ ECs cannot transform into pericytes, as we did not detect any EdU⁺EGFP⁺ pericytes.

(2) The reference for Cdh5CreERT2 is cited as 25, which is a review article published in ATVB. This review lists many different drivers, and the specific Cdh5CreERT2 line used in this study is not identified. This specificity is critical for accurate lineage tracing of ECs.

Although the review I mentioned did not address this, the specificity of Cdh5CreERT2 in the brain has been demonstrated in other studies (Boyé K, et al. Nat Commun. 2022 Mar 4;13(1):1169; Patel A, et al. Proc Natl Acad Sci U S A. 2024 Dec 3;121(49):e2322124121). We have further confirmed that Cdh5CreERT2 specifically labels endothelial cells in the brain parenchyma (Figure S1). Additionally, we found nonspecific labeling in the blood (less than 1% CD45+ blood cells, primarily myeloid cells) and meninges outside the brain parenchyma. We ruled out nonspecific transdifferentiation labeling in the blood through bone marrow reconstitution experiments and in the meninges using in vivo two-photon imaging (results not shown).

(3) The scRNA-seq data should include GFP signals to track the increasing number of pericytes from early to late stages post-injury. This is the only independent method from staining to verify that the pericytes are indeed derived from GFP⁺ ECs after brain injury. Sham samples should be utilized as strict side-by-side controls.

This is a valuable suggestion. We observed that, despite being positive for EGFP protein, only 50% of the sorted cells expressed the EGFP gene at the transcriptome level. This phenomenon has also been reported in other studies (Rodor J,et al a. Cardiovasc Res. 2022 Aug 24;118(11):2519-2534.). For these reasons, we did not rely on GFP signals to track the increase in pericyte numbers from early to late stages post-injury.

(4) Since Ai47 is employed, there are three different variants of green fluorescent proteins, including ZsGreen, which may result in signals being spotted in the staining. The GFP signal detected could also represent dead cells that have lost CD31 expression.

The detected GFP signal could also originate from dead cells that have lost CD31 expression, which is a plausible explanation. As shown in Figure 3I, EGFP⁺ non-ECs peak at RP14D and then decline, suggesting that some EGFP⁺ non-ECs either die or revert to endothelial cells (ECs). Therefore, it cannot be ruled out that we captured some dead EGFP⁺ non-ECs; however, as indicated in Figure 3I, this proportion is likely less than 25%. Additionally, pericytes are prone to death in ischemic and hypoxic environments (Figure 1A), which explains why some of the transformed EGFP⁺ non-ECs may die. Nevertheless, at RP514D, we can still detect EGFP⁺ non-ECs, indicating that a subset of these cells can survive for an extended period (Figure S3F).

(5) The quality of the staining images is not convincing, as some non-ECs and ECs are in close proximity, leading to potential artifacts in signal interpretation. The reviewer cannot rely solely on single staining techniques to be convinced of EC differentiation into pericytes. Although it has been reported that ECs can differentiate into pericytes during development, this phenomenon in the adult brain is surprising; thus, more rigorous evidence with strong lineage tracing data should be provided through multiple measurements.

Why some non-ECs and ECs are located nearby:

(1) Non-ECs exhibit characteristics of pericytes, which are typically adjacent to ECs.

(2) Could this proximity lead to potential artifacts in signal interpretation? We believe this is unlikely, as we also observed a significant number of non-ECs located far from ECs on blood vessels (Figure 3A-B, Figure S3M).

(3) Three pericyte markers (CD13, NG2, and PDGFRβ) were also used to verify the transformed cells, while the three pericyte markers were not expressed in normal endothelial cells.

(6) FACS (Fluorescence-activated cell sorting) should be employed to quantitatively assess the contribution of GFP⁺ ECs to pericytes at each stage after injury, compared to sham controls.

Yes, if the contribution of GFP⁺ ECs to pericytes could be assessed at each time point, the role of E-pericytes in the pericyte pool could be better explained, and the proportion of E-pericytes would become more prominent. In Figure 3, we did not use FACS to evaluate the contribution of GFP⁺ ECs to pericytes at each stage post-injury. Instead, we only assessed the ratio of EGFP⁺ non-ECs to all EGFP⁺ cells. However, we did verify the contribution of GFP⁺ ECs (E-pericytes) to pericytes at RP34D using FACS (CD13+ DsRed/CD13 = 25.6%, Figure 4C). This ratio is consistent with the immunofluorescence data (Figure 3H).

(7) In Tie2Dre;Mfsd2aCrexER;Ai47 mice, ECs in the brain are specifically labeled, indicating that ECs could give rise to CD13+ EGFP⁺ non-ECs at RP34D (Figure S3L). However, the GFP signal for Ai47 is not homogeneous, displaying many spotted patterns. Using tdTomato as an alternative for detection could enhance clarity.

We repeated the experiment using tdTomato as the reporter gene in mice and observed results consistent with those obtained using Ai47 as the reporter gene. For consistency, all results presented are based on Ai47. Regarding the spotted patterns observed with Ai47, this phenomenon can be attributed to the relatively low laser intensity (2%). Higher laser intensity would cause overexposure of EGFP⁺ ECs. To address the issue of spotted patterns in Ai47 imaging, we can improve the visualization of complete cell morphology (as shown in Figure S3M) by increasing the gain value, which enhances the background signal.

(8) The data concerning the genetic ablation of pericytes lacks specificity. There is insufficient evidence to support that DTA is specifically expressed in E-pericytes. The authors should utilize DTR (Diphtheria Toxin Receptor) and confirm that DTR expression is restricted to pericytes derived from GFP⁺ ECs. Treatment with diphtheria toxin, but not PBS as a control, should specifically ablate these E-pericytes without affecting any other GFP-pericytes in the brain following injury.

We did not verify that DTA expression was restricted to E-pericytes. To ensure that DTA is only expressed in converted E-pericytes, we employed two strategies:

(1) Specific Targeting of Endothelial Cells: We used the AAV-BI30 virus to specifically infect endothelial cells. Although not 100% exclusive, 98.5% of the expression occurred in endothelial cells, with minimal infection in neurons and microglia. Additionally, we combined this with Cdh5CreERT2 to control the DIO action in the virus. This means that only endothelial cells expressing both Cdh5CreERT2 and infected with AAV-BI30 could undergo cell fate changes and transform into pericytes, subsequently expressing markers such as NG2 and driving DTA expression in E-pericytes (Figure 4A).

(2) Validation of DTA Expression: To prevent off-target expression of DTA in other cell types, we plan to verify DTA protein expression using specific antibodies to confirm whether DTA is expressed in unintended cells. Alternatively, as suggested, we could utilize the Diphtheria Toxin Receptor (DTR) system. By ensuring that DTR expression is restricted to pericytes derived from GFP⁺ ECs, treatment with diphtheria toxin would specifically ablate these E-pericytes without affecting other GFP- pericytes in the brain post-injury.

(9) There is currently no convincing genetic data demonstrating that Tgfb signaling overexpression or deletion modulates the transdifferentiation of ECs to pericytes.

Yes, this is an important consideration. Although we knocked out the TGFβ receptor in endothelial cells (ECs) and observed a reduction in the formation of E-pericytes (Figure 6D and 6G), it would be more informative to specifically knockout the Tgfb gene in myeloid cells or monocyte-macrophage lineages to determine whether these cells are the primary source of TGFβ driving endothelial cell transformation. Additionally, injecting TGFβ protein directly into the brains of mice could help explore whether exogenous TGFβ promotes the formation of E-pericytes.

Reviewer #2 (Recommendations for the authors):

(1) Figure 1D, there does not appear to be a clear PDGFRβ-positive population. In this case, it is necessary to include the negative control that served as the basis for drawing the positive gate.

Author response image 1 below show the negative control for CD31 and PDGFRβ.

Author response image 1.

(2) Figures 3A-D, Figures S3J-M, the authors statistically compare % negative to % positive. It appears % negative = 100% - % positive. If this is the case, these groups are not independent and should not be statistically compared.

This is a very important point, and such a comparison is not appropriate. The statistical comparison mentioned above has now been removed.

(3) Figure 4B, in addition to the cells indicated with arrows, there is a substantial additional DsRed+ signal of similar intensity in this image. It would be helpful to show a negative control.

Author response image 2 below show the contralateral and ipsilateral, respectively. In the contralateral, DsRed has few signals, no complete cell morphology, and is separated from the Hoechst+ nucleus. in the ipsilateral, DsRed signals are strong, have intact cell morphology, and are tightly bound to the Hoechst+ nucleus. In the ipsilateral, some DsRed signals may come from dying cells.

Author response image 2.

(4) Figure 6G, the y-axis title is "E-pericytes/all EGFP⁺ cells (%)" but the y-axis scale goes from 0 to 900. Is this an error?

Thank you. We want to calculate the number of pericytes per unit area, it should be E-pericyte/mm2.

(5) Figure 9B, in the representative images, the 6th group is labeled "Tgfb2 + DTA" but in the plot below, the 6th group is labeled Tgfbr2 + DsRed. Which is correct?

Thank you. The "Tgfb2 + DTA" is right. We have changed it to "Tgfb2 + DTA" in the 6th group, Figure 9B.

(6) Figure S1I, error bars and/or individual data points should be shown.

The purpose of this diagram is to demonstrate the number of mice in which EGFP⁺ cells are 100% co-labeled with endothelial markers (CD31, ERG, GLUT1, and VE-Cadherin), as EGFP⁺ cells are exclusively found in endothelial cells within the brain parenchyma. Additionally, the diagram illustrates the number of mice in which EGFP⁺ cells show no co-labeling (0%) with mural cell markers (CD13, PDGFRβ, α-SMA, and NG2), as EGFP⁺ cells are not present in mural cells within the brain parenchyma.

(7) The authors write: "When Tgfbr2 was overexpressed and DTA was expressed specifically in the same ECs, DTA prevented the EC-specific overexpression of the Tgfbr2 gene and increased the proportion of E-pericytes.". The authors' strategy for DTA expression involves the NG2 promoter, which, in principle, is not active in ECs. Thus how can DTA be "expressed specifically in the same ECs" and how can DTA "prevent EC-specific overexpression" of Tgfbr2?

Our purpose is not clearly expressed. The statement should be revised to: “When Tgfbr2 was overexpressed to increase E-pericytes and DTA was expressed in transformed cells to deplete E-pericytes, we found that there was no significant change in the number of E-pericytes in the Tgfbr2 + DTA group compared with the DTA group.”

(8) The interpretation of Evans blue leakage as "low molecular weight" leakage should be revised since Evans blue binds serum albumin and thus it is the molecular weight of this complex (~67 kDa) that is relevant.

We agree with the reviewer. Yes, it should not be stated that Evans blue is low molecular weight, as it binds to serum albumin to form complexes. The text has been revised to: “Interestingly, no obvious leakage of dextran-rhodamine B (~70 kDa) (Figure S8C) or Texas Red (~71 kDa) was detected (Figure S8D). However, the elimination of E-pericytes allowed evans blue and trypan blue to cross the blood-brain barrier (BBB).”

(9) It is critical that the sequencing data be made available through a public repository (such as GEO).

Thank you. Now we've uploaded it to GEO.

(10) It would be extremely helpful if the authors would make their viral plasmids available through a public repository (such as Addgene).

Thank you. Now we've uploaded it to Addgene (The assignment of Addgene number is pending).

Reviewer #3 (Recommendations for the authors):

(1) The distribution and expression of pericytic and fibroblast markers at different time points after stroke is confusing while reading the manuscript, e.g., vimentin is not expressed on day 34 but on day 8, whereas CD13 is expressed on day 34 but not on day 8, if I understood the text correctly. To make it easier to follow, the authors could add a label of the day after stroke to each of the subfigures which show images and co-expression of different markers (e.g. Figures 3 and S3).

Below are the expressions of different specific markers in each cell.

“√” stand for positive, “×” stand for positive

Author response table 1.

(2) The authors need to check the N numbers again, e.g., Figure S3L: 4 dots per group are shown in the graph but an N of 3 is mentioned in the legend.

Thank you for raising this important point. N=4 has been corrected in the legend of Figure 3S. We also checked other N numbers.

(3) Labelling of graphs should be consistent (e.g., S4C: "I-ECs" vs. S4F: "Ipsi-ECs") and correct (e.g., "DsRed" instead of "DeRed" in Figure 4B).

Yes, we need a uniform name with "Ipsi-ECs" and "DsRed". Thank you.

(4) Figure 4: In the text, the injection is described to be done on day 34 whereas in Figure 4A the injections are described to take place before MCAO, please clarify. Does day 34 mean 34 days after injection or after MCAO (as in the former experiments)?

In the text, the sentence, “Then we used AAV2/9-BI30-NG2 promoter-DIO-DTA (DTA) to deplete E-pericytes at RP34D (Figure 4D),” could be misinterpreted as suggesting that the virus was injected at RP34D. To avoid confusion, it has been revised to: “We used the AAV2/9-BI30-NG2 promoter-DIO-DTA (DTA) virus, which was injected before MCAO (Figure 4A), to deplete E-pericytes (Figure 4D).” Yes, day 34 means 34 days after injection or after MCAO and we unify to 34 days.

(5) Some images are too dark to recognize clear structures and prove the findings (e.g., Figure S6B).

Thank you for raising this important point.

(6) There is no Figure S8D (as mentioned in the text).

Thank you for raising this important point. This problem has been corrected.

(7) Figure S9: the text only states, that Tgfbr2 overexpression increases CBF recovery and effective perfusion. Also with the legend, it is not clear what was done and measured, especially in Figure S9B - what do the graphs show? Also, the y-axis labeling is missing for the traces.

In Figure S9A, we assessed changes in blood flow using laser speckle imaging. Laser speckle imaging relies on random interference patterns formed by scattered light when a laser strikes tissue. Moving red blood cells alter the contrast of the speckle pattern: faster blood flow results in quicker speckle changes and lower contrast, while slower blood flow leads to slower speckle changes and higher contrast. By analyzing these changes in speckle contrast, blood flow dynamics can be evaluated in real-time and non-invasively.

In Figure S9B, we measured blood flow changes using Laser Doppler flowmetry. When a laser interacts with flowing blood, the moving red blood cells scatter the light, causing a frequency shift (Doppler shift). Faster blood flow results in a greater frequency shift, while slower blood flow leads to a smaller frequency shift. By detecting the frequency shift of the scattered light, blood flow velocity and changes can be measured in real time and non-invasively. In Laser Doppler Flowmetry (LDF), the unit of the vertical axis is typically Perfusion Units (PU). PU is a relative unit used to represent changes in blood flow rather than absolute blood flow velocity. These methods have now been further explained in the diagram.

(8) Which regions of the brain were used to take images (e.g., to count neurons)?

We captured images and quantified neurons in the cortex and striatum of the brain. Our statistical analysis further demonstrated that, at RP34D, the presence of E-pericytes in the brain does not exhibit region-specificity. Instead, the formation of E-pericytes is driven by TGFβ1, which is regulated by immune cells. Ultimately, the distribution and activity of these immune cells are influenced by the severity of ischemia and hypoxia.

(9) The sentence "Protein C receptor-expressing (Procr+) ECs could give rise to de novo formation of ECs and pericytes in the mammary gland13." is repeated almost identically in three different places in the text. However, whether Procr+ cells are involved in the described transdifferentiation or whether "E-pericytes" do express the protein C receptor is not shown and needs additional investigation.

The reason for referencing this literature is to highlight that endothelial cells (ECs) during breast development can give rise to pericytes, which serves as background knowledge supporting our research. To further explore this phenomenon in brain, we used ProcrCreERT2;Ai47 mice subjected to MCAO (middle cerebral artery occlusion) to investigate whether Procr+ ECs could transform into pericytes, similar to what occurs in mammary glands. However, since ProcrCreERT2 labels not only ECs but also pericytes in the brain, the results did not achieve our goal and were therefore not included in the study.

Author response:

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

Reviewer #1 (Public Review):

Summary:  

This paper investigates the relationship between ocular drift - eye movements long thought to be random - and visual acuity. This is a fundamental issue for how vision works. The work uses adaptive optics retinal imaging to monitor eye movements and where a target object is in the cone photoreceptor array. The surprising result is that ocular drift is systematic - causing the object to move to the center of the cone mosaic over the course of each perceptual trial. The tools used to reach this conclusion are state-of-the-art and the evidence presented is convincing.

Strengths  

P1.1. The central question of the paper is interesting, as far as I know, it has not been answered in past work, and the approaches employed in this work are appropriate and provide clear answers.

P1.2. The central finding - that ocular drift is not a completely random process - is important and has a broad impact on how we think about the relationship between eye movements and visual perception.

P1.3. The presentation is quite nice: the figures clearly illustrate key points and have a nice mix of primary and analyzed data, and the writing (with one important exception) is generally clear.

Thank you for your positive feedback.

Weaknesses

P1.4. The handling of the Nyquist limit is confusing throughout the paper and could be improved. It is not clear (at least to me) how the Nyquist limit applies to the specific task considered. I think of the Nyquist limit as saying that spatial frequencies above a certain cutoff set by the cone spacing are being aliased and cannot be disambiguated from the structure at a lower spatial frequency. In other words, there is a limit to the spatial frequency content that can be uniquely represented by discrete cone sampling locations. Acuity beyond that limit is certainly possible with a stationary image - e.g. a line will set up a distribution of responses in the cones that it covers, and without noise, an arbitrarily small displacement of the line would change the distribution of cone responses in a way that could be resolved. This is an important point because it relates to whether some kind of active sampling or movement of the detectors is needed to explain the spatial resolution results in the paper. This issue comes up in the introduction, results, and discussion. It arises in particular in the two Discussion paragraphs starting on line 343.

We thank you for pointing out a possible confusion for readers. Overall, we contrast our results to the static Nyquist limit because it is generally regarded as the upper limit of resolution acuity. We updated our text in a few places, especially the Discussion, and added a reference to make our use of the Nyquist limit clearer.

We agree with the reviewer of how the Nyquist limit is interpreted within the context of visual structure. If visual structure is under-sampled, it is not lost, but creates new, interfered visual structure at lower spatial frequency. For regular patterns like gratings, interference patterns may emerge akin to Moire patterns, which have been shown to occur in the human eye, and which form is based on the arrangement and regularity of the photoreceptor mosaic (Williams, 1985). We note however that the successful resolution of the lower frequency pattern does not necessarily carry the same structural information, specifically, orientation, and the aliased structure might indeed mask the original stimulus. Please compare Figure 1f where we show individual static snapshots of such aliased patterns, especially visible when the optotypes are small (towards the lower right of the figure). We note that theoretical work predicts that with prior knowledge about the stimulus, even such static images might be possible to de-alias (Ruderman & Bialek, 1992). We added this to our manuscript.   

We think the reviewer’s following point about the resolution of a line position, is only partially connected to the first, however. In our manuscript we note in the Introduction that resolution of the relative position of visual objects is a so called hyperacuity phenomenon. The fact that it occurs in humans and other animals demonstrates that visual brains have come up with neuronal mechanisms to determine relative stimulus position with sub-Nyquist resolution. The exact mechanism is however not fully clear. One solution is that relative cone signal intensities could be harnessed, similar as is employed technically, e.g. in a quadrant-cell detector. Its positional precision is much higher than the individual cell’s size (or Nyquist limit), predominantly determined by the detector’s sensitivity and to a lesser degree its size. On the other hand, such detector, being hyperacute with object location, would not have the same resolution as, for instance, letter-E orientation discrimination. 

Note that in all the above occasions, a static image-sensor-relationship is assumed. In our paper, we were aiming to convey, like others did before, that a moving stimulus may give rise to sub-Nyquist structural resolution, beyond what is already known for positional acuity and hence, classical hyperacuity. 

Based on the data shown in this manuscript and other experimental data currently collected in the lab, it seems to us that eye movements are indeed the crucial point in achieving sub-Nyquist resolution. For example, ultra-short presentation durations, allowing virtually no retinal slip, push thresholds close to the Nyquist limit and above. Furthermore, with AOSLO stimulation, it is possible to stabilize a stimulus on the retina, which would be a useful tool studying this hypothesis. Our current level of stabilization is however not accurate enough to completely mitigate retinal image motion in the foveola, where cells are smallest, and transients could occur. From what we observe and other studies that looked at resolution thresholds at more peripheral retinal locations, we would predict that foveolar resolution of a perfectly stabilized stimulus would be indeed limited by the Nyquist limit of the receptor mosaic.

P1.5. One question that came up as I read the paper was whether the eye movement parameters depend on the size of the E. In other words, to what extent is ocular drift tuned to specific behavioral tasks?

This is an interesting question. Yet, the experimental data collected for the current manuscript does not contain enough dispersion in target size to give a definitive answer, unfortunately. A larger range of stimulus sizes and especially a similar number of trials per size would be required. Nonetheless, when individual trials were re-grouped to percentiles of all stimulus sizes (scaled for each eye individually), we found that drift length and directionality was not significantly different between any percentile group of stimulus sizes (Wilcoxon sign rank test, p > 0.12, see also Figure R1). Our experimental trials started with a stimulus demanding visual acuity of 20/16 (logMAR = -0.1), therefore all presented stimulus sizes were rather close to threshold. The high visual demand in this AO resolution task might bring the oculomotor system to a limit, where ocular drift length can’t be decreased further. However, with the limitation due to the small range of stimulus sizes, further investigations would be needed. Given this and that this topic is also ongoing research in our lab where also more complex dynamics of FEM patterns are considered, we refrain from showing this analysis in the current manuscript.  

Author response image 1.

Drift length does not depend on stimulus sizes close to threshold. All experimental trials were sorted by stimulus size and then grouped into percentiles for each participant (left). Additionally, 10 % of trials with stimulus sizes just above or below threshold are shown for comparison (right). For each group, median drift lengths (z-scored) are shown as box and whiskers plot. Drift length was not significantly different across groups.  

Reviewer #2 (Public Review):

Summary:

In this work, Witten et al. assess visual acuity, cone density, and fixational behavior in the central foveal region in a large number of subjects.

This work elegantly presents a number of important findings, and I can see this becoming a landmark work in the field. First, it shows that acuity is determined by the cone mosaic, hence, subjects characterized by higher cone densities show higher acuity in diffraction-limited settings. Second, it shows that humans can achieve higher visual resolution than what is dictated by cone sampling, suggesting that this is likely the result of fixational drift, which constantly moves the stimuli over the cone mosaic. Third, the study reports a correlation between the amplitude of fixational motion and acuity, namely, subjects with smaller drifts have higher acuities and higher cone density. Fourth, it is shown that humans tend to move the fixated object toward the region of higher cone density in the retina, lending further support to the idea that drift is not a random process, but is likely controlled. This is a beautiful and unique work that furthers our understanding of the visuomotor system and the interplay of anatomy, oculomotor behavior, and visual acuity.

Strengths:

P2.1. The work is rigorously conducted, it uses state-of-the-art technology to record fixational eye movements while imaging the central fovea at high resolution and examines exactly where the viewed stimulus falls on individuals' foveal cone mosaic with respect to different anatomical landmarks in this region. The figures are clear and nicely packaged. It is important to emphasize that this study is a real tour-de-force in which the authors collected a massive amount of data on 20 subjects. This is particularly remarkable considering how challenging it is to run psychophysics experiments using this sophisticated technology. Most of the studies using psychophysics with AO are, indeed, limited to a few subjects. Therefore, this work shows a unique set of data, filling a gap in the literature.

Thank you, we are very grateful for your positive feedback.

Weaknesses:

P2.2. No major weakness was noted, but data analysis could be further improved by examining drift instantaneous direction rather than start-point-end-point direction, and by adding a statistical quantification of the difference in direction tuning between the three anatomical landmarks considered.

Thank you for these two suggestions. We now show the development of directionality with time (after the first frame, 33 ms as well as 165 ms, 330 ms and 462 ms), and performed a Rayleigh test for non-uniformity of circular data. Please also see our response to comment R2.4.

Briefly, directional tuning was already visible at 33 ms after stimulus onset and continuously increases with longer analysis duration. Directionality is thus not pronounced at shorter analysis windows. These results have been added to the text and figures (Figure 4 - figure supplement 1).

The statistical tests showed that circular sample directionality was not uniformly distributed for all three retinal locations. The circular average was between -10 and 10 ° in all cases and the variance was decreasing with increasing time (from 48.5 ° to 34.3 ° for CDC, 49.6 ° to 38.6 ° for PRL and 53.9 ° to 43.4 for PCD location, between frame 2 and 15). As we have discussed in the paper, we would expect all three locations to come out as significant, given their vicinity to the CDC (which is systematic in the case of PRL, and random in the case of PCD, see also comment R2.2).        

Reviewer #3 (Public Review):

Summary:

The manuscript by Witten et al., titled "Sub-cone visual resolution by active, adaptive sampling in the human foveola," aims to investigate the link between acuity thresholds (and hyperacuity) and retinal sampling. Specifically, using in vivo foveal cone-resolved imaging and simultaneous microscopic photostimulation, the researchers examined visual acuity thresholds in 16 volunteers and correlated them with each individual's retinal sampling capacity and the characteristics of ocular drift.

First, the authors found that although visual acuity was highly correlated with the individual spatial arrangement of cones, for all participants, visual resolution exceeded the Nyquist sampling limit - a well-known phenomenon in the literature called hyperacuity.

Thus, the researchers hypothesized that this increase in acuity, which could not be explained in terms of spatial encoding mechanisms, might result from exploiting the spatiotemporal characteristics of visual input, which is continuously modulated over time by eye movements even during so-called fixations (e.g., ocular drift).

Authors reported a correlation between subjects, between acuity threshold and drift amplitude, suggesting that the visual system benefits from transforming spatial input into a spatiotemporal flow. Finally, they showed that drift, contrary to the traditional view of it as random involuntary movement, appears to exhibit directionality: drift tends to move stimuli to higher cone density areas, therefore enhancing visual resolution.

Strengths:

P3.1. The work is of broad interest, the methods are clear, and the results are solid.

Thank you.

Weaknesses:

P3.2. Literature (1/2): The authors do not appear to be aware of an important paper published in 2023 by Lin et al. (https://doi.org/10.1016/j.cub.2023.03.026), which nicely demonstrates that (i) ocular drifts are under cognitive influence, and (ii) specific task knowledge influences the dominant orientation of these ocular drifts even in the absence of visual information. The results of this article are particularly relevant and should be discussed in light of the findings of the current experiment.

Thank you for pointing to this important work which we were aware of. It simply slipped through during writing. It is now discussed in lines 390-393. 

P3.3. Literature (2/2): The hypothesis that hyperacuity is attributable to ocular movements has been proposed by other authors and should be cited and discussed (e.g., https://doi.org/10.3389/fncom.2012.00089, https://doi.org/10.10

Thank you for pointing us towards these works which we have now added to the Discussion section. We would like to stress however, that we see a distinction between classical hyperacuity phenomena (Vernier, stereo, centering, etc.) as a form of positional acuity, and orientation discrimination.  

P3.4. Drift Dynamic Characterization: The drift is primarily characterized as the "concatenated vector sum of all frame-wise motion vectors within the 500 ms stimulus duration.". To better compare with other studies investigating the link between drift dynamics and visual acuity (e.g., Clark et al., 2022), it would be interesting to analyze the drift-diffusion constant, which might be the parameter most capable of describing the dynamic characteristics of drift.

During our analysis, we have computed the diffusion coefficient (D) and it showed qualitatively similar results to the drift length (see figures below). We decided to not show these results, because we are convinced that D is indeed not the most capable parameter to describe the typical drift characteristic seen here. The diffusion coefficient is computed as the slope of the mean square displacement (MSD). In our view, there are two main issues with applying this metric to our data, one conceptual, one factual:

(1) Computation of a diffusion coefficient is based upon the assumption that the underlying movement is similar to a random walk process. From a historical perspective, where drift has been regarded as more random, this makes sense. We also agree that D can serve as a valuable metric, depending on the individual research question. In our data, however, we clearly show that drift is not random, and a metric quantifying randomness is thus ill-defined. 

(2) We often observed out- and in-type motion traces, i.e. where the eye somewhat backtracks from where it started. Traces in this case are equally long (and fast) as other motion will be with a singular direction, but D would in this case be much smaller, as the MSD first increases and then decreases. In reality, the same number of cones would have been traversed as with the larger D of straight outward movement, albeit not unique cones. For our current analyses, the drift length captures this relationship better.

Author response image 2.

Diffusion coefficient (D) and the relation to visual acuity (see Figure 3 e-g for comparison to drift length). a, D was strongly correlated between fellow eyes. b, Cone density and D were not significantly correlated. c, The median D had a moderate correlation with visual acuity thresholds in dominant as well as non-dominant eyes. Dominant eyes are indicated by filled, nondominant eyes by open markers.

We would like to put forward that, in general, better metrics are needed, especially in respect to the visual signals arising from the moving eye. We are actively looking into this in follow-up work, and we hope that the current manuscript might spark also others to come up with new ways of characterizing the fine movements of the eye during fixation.

P3.5. Possible inconsistencies: Binocular differences are not expected based on the hypothesis; the authors may speculate a bit more about this. Additionally, the fact that hyperacuity does not occur with longer infrared wavelengths but the drift dynamics do not vary between the two conditions is interesting and should be discussed more thoroughly.

Binocularity: the differences in performance between fellow eyes is rather subtle, and we do not have a firm grip on differences other than the cone mosaic and fixational motor behavior between the two eyes. We would rather not speculate beyond what we already do, namely that some factor related to the development of ocular dominance is at play. What we do show with our data is that cone density and drift patterns seem to have no part in it.  

Effect of wavelength: even with the longer 840 nm wavelength, most eyes resolve below the Nyquist limit, with a general increase in thresholds (getting worse) compared to 788 nm. As we wrote in the manuscript, we assume that the increased image blur and reduced cone contrast introduced by the longer wavelength are key to why there is an overall reduction in acuity. No changes were made to the manuscript. As a more general remark, we would not consider the sub-Nyquist performances seen in our data to be a hyperacuity, although technically it is. The reason is that hyperacuity is usually associated with stimuli that require resolving positional shifts, and not orientation. There is a log unit of difference between thresholds in these tasks.  

P3.6. As a Suggestion: can the authors predict the accuracy of individual participants in single trials just by looking at the drift dynamics?

That’s a very interesting point that we indeed currently look at in another project. As a comment, we can add that by purely looking at the drift dynamics in the current data, we could not predict the accuracy (percent correct) of the participant. When comparing drift length or diffusion coefficients between trials with correct or false response, we do not observe a significant difference. Also, when adding an anatomical correlate and compare between trials where sampling density increases or decreases, there is no significant trend. We think that it is a more complex interplay between all the influencing factors that can perhaps be met by a model considering all drift dynamics, photoreceptor geometry and stimulus characteristics.   

No changes were made to the manuscript.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

As you will see, the reviewers were quite enthusiastic about your work, but have a few issues for your consideration. We hope that this is helpful. We'll consider any revisions in composing a final eLife assessment.

Reviewer #1 (Recommendations For The Authors):

R1.1:  Discussion of myopia. Myopia takes a fair bit of space in the Discussion, but the paper does not include any subjects that are sufficiently myopic to test the predictions. I would suggest reducing the amount of space devoted to this issue, and instead making the prediction that myopia may help with resolution quickly. The introduction (lines 54-56) left me expecting a test of this hypothesis, and I think similarly that issue could be left out of the introduction.

We have removed this part from the Introduction and shortened the Discussion.  

R1.2: Line 118: define CDC here.

Thank you for pointing this out, it is now defined at this location.  

R1.3: Line 159-162: suggest breaking this sentence into two. This sentence also serves as a transition to the next section, but the wording suggests it is a result that is shown in the prior section. Suggest rewording to make the transition part clear. Maybe something like "Hence the spatial arrangement of cones only partially ... . Next we show that ocular motion and the associated ... are another important factor."

Text was changed as suggested.  

R1.4.: Figure 3: The retina images are a bit hard to see - suggest making them larger to take an entire row. As a reader, I also was wondering about the temporal progression of the drift trajectories and the relation to the CDC. Since you get to that in Figure 4, you could clarify in the text that you are starting by analyzing distance traveled and will return to the issue of directed trajectories.

Visibility was probably an issue during the initial submission and review process where images were produced at lower resolution. The original figures are of sufficient resolution to fully appreciate the underlying cone mosaic and will later be able to zoom in the online publication.  

We added a mention of the order of analysis in the Results section (LL 163-165)

R1.5: Line 176: define "sum of piecewise drift amplitude" (e.g. refer to Figure where it is defined).

We refer to this metric now as the drift length (as pointed out rightfully so by reviewer #2), and added its definition at this location.   

R1.6: Lines 205-208: suggest clarifying this sentence is a transition to the next section. As for the earlier sentence mentioned above, this sounds like a result rather than a transition to an issue you will consider next.

This sentence was changed to make the transition clearer. 

R1.7: Line 225: suggest starting a new paragraph here.

Done as suggested

Reviewer #2 (Recommendations For The Authors):

I don't have any major concerns, mostly suggestions and minor comments.

R2.1: (1) The authors use piecewise amplitude as a measure of the amount of retinal motion introduced by ocular drift. However, to me, this sounds like what is normally referred to as the path length of a trace rather than its amplitude. I would suggest using the term length rather than amplitude, as amplitude is normally considered the distance between the starting and the ending point of a trace.

This was changed as suggested throughout the manuscript. 

R2.2: (2) It would be useful to elaborate more on the difference between CDC and PCD, I know the authors do this in other publications, but to the naïve reader, it comes a bit as a surprise that drift directionality is toward the CDC but less so toward the PCD. Is the difference between these metrics simply related to the fact that defining the PCD location is more susceptible to errors, especially if image quality is not optimal? If indeed the PCD is the point of peak cone density, assuming no errors or variability in the estimation of this point, shouldn't we expect drift moving stimuli toward this point, as the CDC will be characterized by a slightly lower density? I.e., is the absence of a PCD directionality trend as strong as the trend seen for the CDC simply the result of variability and error in the estimate of the PCD or it is primarily due to the distribution of cone density not being symmetrical around the PCD?

Thank you for this comment. We already refer in the Methods section to the respective papers where this difference is analyzed in more detail, and shortly discuss it here.

To briefly answer the reviewer’s final question: PCD location is too variable, and ought to be avoided as a retinal landmark. While we believe there is value in reporting the PCD as a metric of maximum density, it has been shown recently (Reiniger et al., 2021; Warr et al., 2024; Wynne et al., 2022) and is visible in our own (partly unpublished) data, that its location will change with changing one or more of these factors: cone density metric, window size or cone quantity selected, cone annotation quality, image quality (e.g. across days), individual grader, annotation software, and likely more. Each of these factors alone can change the PCD location quite drastically, all while of course, the retina does not change. The CDC on the other hand, given its low-pass filtering nature, is immune to the aforementioned changes within a much wider range and will thus reflect the anatomical and, shown here, functional center of vision, better. However, there will always be individual eyes where PCD location and the CDC are close, and thus researchers might be inclined to also use the PCD as a landmark. We strongly advise against this. In a way, the PCD is a non-sense location while its dimension, density, can be a valuable metric, as density does not vary that much (see e.g. data on CDC density and PCD density reported in this manuscript).  

Below we append a direct comparison of PCD vs CDC location stability when only one of the mentioned factors are changed. Sixteen retinas imaged on two different days were annotated and analyzed by the same grader with the same approach, and the difference in both locations are shown.  

Author response image 3.

Reproducibility of CDC and PCD location in comparison. Two retinal mosaics which were recorded at two different timepoints, maximum 1 year apart from each other, were compared for 16 eyes. The retinal mosaics were carefully aligned. The retinal locations for CDC and PCD that were computed for the first timepoint were used as the spatial anchor (coordinate center), the locations plotted here as red circles (CDC) and gray diamonds (PCD) represent the deviations that were measured at the second timepoint for both metrics.  

R2.3.: I don't see a statistical comparison between the drift angle tuning for CDC, PRL, and PCD. The distributions in Figure 4F look very similar and all with a relatively wide std. It would be useful to mark the mean of the distributions and report statistical tests. What are the data shown in this figure, single subjects, all subjects pooled together, average across subjects? Please specify in the caption.

We added a Rayleigh test to test each distribution for nun-uniformity and Kolmogorov-Smirnov tests to compare the distributions towards the different landmarks.  We added the missing specifications to the figure caption of Figure 4 – figure supplement 1. 

R2.4: I would suggest also calculating drift direction based on the average instantaneous drift velocity, similarly to what is done with amplitude. From Figure 3B it is clear that some drifts are more curved than others. For curved drifts with small amplitudes the start-point- end-point (SE) direction is not very meaningful and it is not a good representation of the overall directionality of the segment. Some drifts also seem to be monotonic and then change direction (eg. the last three examples from participant 10). In this case, the SE direction is likely quite different from the average instantaneous direction. I suspect that if direction is calculated this way it may show the trend of drifting toward the CDC more clearly.

In response to this and a comment of reviewer #1, we add a calculation of initial  drift direction (and for increasing duration) and show it in Figure 4 – figure supplement 1. By doing so, we hope to capture initial directionality, irrespective of whether later parts in the path change direction. We find that directionality increases with increasing presentation duration. 

R2.5: I find the discussion point on myopia a bit confusing. Considering that this is a rather tangential point and there are only two myopic participants, I would suggest either removing it from the discussion or explaining it more clearly.

We changed this section, also in response to comment R1.1.

R2.6: I would suggest adding to the discussion more elaboration on how these results may relate to acuity in normal conditions (in the presence of optical aberrations). For example, will this relationship between sampling cone density and visual acuity also hold natural viewing conditions?

We added only a half sentence to the first paragraph of the discussion. We are hesitant to extend this because there is very likely a non-straightforward relationship between acuity in normal and fully corrected conditions. We would predict that, if each eye were given the same type and magnitude of aberrations (similar to what we achieved by removing them), cone density will be the most prominent factor of acuity differences. Given that individual aberrations can vary substantially between eyes, this effect will be diluted, up to the point where aberrations will be the most important factor to acuity. As an example, under natural viewing conditions, pupil size will dominantly modulate the magnitude of aberrations.

R2.7: Line 398 - the point on the superdiffusive nature of drift comes out of the blue and it is unclear. What is it meant by "superdiffusive"?

We simply wanted to express that some drift properties seem to be adaptable while others aren’t. The text was changed at this location to remove this seemingly unmotivated term. 

R2.8: Although it is true that drift has been assumed to be a random motion, there has been mounting evidence, especially in recent years, showing a degree of control and knowledge about ocular drift (eg. Poletti et al, 2015, JN; Lin et al, 2023, Current Biology).

We agree, of course. We mention this fact several times in the paper and adjusted some sentences to prevent misunderstandings. The mentioned papers are now cited in the Discussion. 

R2.9: Reference 23 is out of context and should be removed as it deals with the control of fine spatial attention in the foveola rather than microsaccades or drift.

We removed this reference. 

R2.10: Minor point: Figures appear to be low resolution in the pdf.

This seemed to have been an issue with the submission process. All figures will be available in high resolution in the final online version. 

R2.11: Figure S3, it would be useful to mark the CDC at the center with a different color maybe shaded so it can be visible also on the plot on the left.

We changed the color and added a small amount of transparency to the PRL markers to make the CDC marker more visible. 

R2.12: Figure S2, it would be useful to show the same graphs with respect to the PCD and PRL and maybe highlight the subjects who showed the largest (or smallest) distance between PRL and CDC).

Please find new Figure 4 supplement 1, which contains this information in the group histograms. Also, Figure 4 supplement 2 is now ordered by the distance PRL-CDC (while the participant naming is kept as maximum acuity exhibited. In this way, it should be possible to infer the information of whether PRL-CDC distance plays a role. For us it does not seem to be crucial. Rather, stimulus onset and drift length were related, which is captured in Figure 4g. 

R2.13: There is a typo in Line 410.

We could not find a typo in this line, nor in the ones above and below. “Interindividual” was written on purpose, maybe “intraindividual” was expected? No changes were made to the text. 

References

Reiniger, J. L., Domdei, N., Holz, F. G., & Harmening, W. M. (2021). Human gaze is systematically offset from the center of cone topography. Current Biology, 31(18), 4188–4193. https://doi.org/10.1016/j.cub.2021.07.005

Ruderman, D. L., & Bialek, W. (1992). Seeing Beyond the Nyquist Limit. Neural Computation, 4(5), 682–690. https://doi.org/10.1162/neco.1992.4.5.682

Warr, E., Grieshop, J., Cooper, R. F., & Carroll, J. (2024). The effect of sampling window size on topographical maps of foveal cone density. Frontiers in Ophthalmology, 4, 1348950. https://doi.org/10.3389/fopht.2024.1348950

Williams, D. R. (1985). Aliasing in human foveal vision. Vision Research, 25(2), 195–205. https://doi.org/10.1016/0042-6989(85)90113-0

Wynne, N., Cava, J. A., Gaffney, M., Heitkotter, H., Scheidt, A., Reiniger, J. L., Grieshop, J., Yang, K., Harmening, W. M., Cooper, R. F., & Carroll, J. (2022). Intergrader agreement of foveal cone topography measured using adaptive optics scanning light ophthalmoscopy. Biomedical Optics Express, 13(8), 4445–4454. https://doi.org/10.1364/boe.460821

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The manuscript by Mäkelä et al. presents compelling experimental evidence that the amount of chromosomal DNA can become limiting for the total rate of mRNA transcription and consequently protein production in the model bacterium Escherichia coli. Specifically, the authors demonstrate that upon inhibition of DNA replication the single-cell growth rate continuously decreases, in direct proportion to the concentration of active ribosomes, as measured indirectly by single-particle tracking. The decrease of ribosomal activity with filamentation, in turn, is likely caused by a decrease of the concentration of mRNAs, as suggested by an observed plateau of the total number of active RNA polymerases. These observations are compatible with the hypothesis that DNA limits the total rate of transcription and thus translation. The authors also demonstrate that the decrease of RNAp activity is independent of two candidate stress response pathways, the SOS stress response and the stringent response, as well as an anti-sigma factor previously implicated in variations of RNAp activity upon variations of nutrient sources.

Remarkably, the reduction of growth rate is observed soon after the inhibition of DNA replication, suggesting that the amount of DNA in wild-type cells is tuned to provide just as much substrate for RNA polymerase as needed to saturate most ribosomes with mRNAs. While previous studies of bacterial growth have most often focused on ribosomes and metabolic proteins, this study provides important evidence that chromosomal DNA has a previously underestimated important and potentially rate-limiting role for growth. 

Thank you for the excellent summary of our work.

Strengths: 

This article links the growth of single cells to the amount of DNA, the number of active ribosomes and to the number of RNA polymerases, combining quantitative experiments with theory. The correlations observed during depletion of DNA, notably in M9gluCAA medium, are compelling and point towards a limiting role of DNA for transcription and subsequently for protein production soon after reduction of the amount of DNA in the cell. The article also contains a theoretical model of transcription-translation that contains a Michaelis-Menten type dependency of transcription on DNA availability and is fit to the data. While the model fits well with the continuous reduction of relative growth rate in rich medium (M9gluCAA), the behavior in minimal media without casamino acids is a bit less clear (see comments below). 

At a technical level, single-cell growth experiments and single-particle tracking experiments are well described, suggesting that different diffusive states of molecules represent different states of RNAp/ribosome activities, which reflect the reduction of growth. However, I still have a few points about the interpretation of the data and the measured fractions of active ribosomes (see below). 

Apart from correlations in DNA-deplete cells, the article also investigates the role of candidate stress response pathways for reduced transcription, demonstrating that neither the SOS nor the stringent response are responsible for the reduced rate of growth. Equally, the anti-sigma factor Rsd recently described for its role in controlling RNA polymerase activity in nutrient-poor growth media, seems also not involved according to mass-spec data. While other (unknown) pathways might still be involved in reducing the number of active RNA polymerases, the proposed hypothesis of the DNA substrate itself being limiting for the total rate of transcription is appealing. 

Finally, the authors confirm the reduction of growth in the distant Caulobacter crescentus, which lacks overlapping rounds of replication and could thus have shown a different dependency on DNA concentration. 

Weaknesses: 

There are a range of points that should be clarified or addressed, either by additional experiments/analyses or by explanations or clear disclaimers. 

First, the continuous reduction of growth rate upon arrest of DNA replication initiation observed in rich growth medium (M9gluCAA) is not equally observed in poor media. Instead, the relative growth rate is immediately/quickly reduced by about 10-20% and then maintained for long times, as if the arrest of replication initiation had an immediate effect but would then not lead to saturation of the DNA substrate. In particular, the long plateau of a constant relative growth rate in M9ala is difficult to reconcile with the model fit in Fig 4S2. Is it possible that DNA is not limiting in poor media (at least not for the cell sizes studied here) while replication arrest still elicits a reduction of growth rate in a different way? Might this have something to do with the naturally much higher oscillations of DNA concentration in minimal medium?

The reviewer is correct that there are interesting differences between nutrient-rich and -poor conditions. They were originally noted in the discussion, but we understand how our original presentation made it confusing. We reorganized the text and figures to better explain our results and interpretations. In the revised manuscript, the data related to the poor media are now presented separately (new Figure 6) from the data related to the rich medium (Figures 1-3).  The total RNAP activity (abundance x active fraction) is significantly reduced in poor media (Figure 6A-B) similarly to rich medium (Figure 3H). Thus, DNA is limiting for transcription across conditions. However, the total ribosome activity in poor media (Figure 6C-D) and thus the growth rate (Figure 6EF) was less affected in comparison to rich media (Figure 2H and 1C). Our interpretation of these results is that while DNA is limiting for transcription in all tested nutrient conditions (as shown by the total active RNAP data), post-transcriptional buffering activities compensate for the reduction in transcription in poor media, thereby maintaining a better scaling of growth rates under DNA limitation. 

The authors argue that DNA becomes limiting in the range of physiological cell sizes, in particular for M9glCAA (Fig. 1BC). It would be helpful to know by how much (fold-change) the DNA concentration is reduced below wild-type (or multi-N) levels at t=0 in Fig 1B and how DNA concentration decays with time or cell area, to get a sense by how many-fold DNA is essentially 'overexpressed/overprovided' in wild-type cells. 

We now provide crude estimates in the Discussion section. The revised text reads: “Crude estimations suggest that ≤ 40% DNA dilution is sufficient to negatively affect transcription (total RNAP activity) in M9glyCAAT, whereas the same effect was observed after less than 10% dilution in nutrient-poor media (M9gly or M9ala) (see Materials and Methods).” We obtained these numbers based on calculations and estimates described in the Materials and Methods section and Appendix 1 (Appendix 1 – Table 1).

Fig. 2: The distribution of diffusion coefficients of RpsB is fit to Gaussians on the log scale. Is this based on a model or on previous work or simply an empirical fit to the data? An exact analytical model for the distribution of diffusion constants can be found in the tool anaDDA by Vink, ..., Hohlbein Biophys J 2020. Alternatively, distributions of displacements are expressed analytically in other tools (e.g., in SpotOn). 

We use an empirical fit of Gaussian mixture model (GMM) of three states to the data and extract the fractions of molecules in each state. This avoids making too many assumptions on the underlying processes, e.g. a Markovian system with Brownian diffusion. The model in anaDDA (Vink et al.) is currently limited to two-transitioning states with a maximal step number of 8 steps per track for a computationally efficient solution (longer tracks are truncated). Using a short subset of the trajectories is less accurate than using the entire trajectory and because of this, we consider full tracks with at least 9 displacements. Meanwhile, Spot-On supports a three-state model but it is still based on a semi-analytical model with a pre-calculated library of parameters created by fitting of simulated data. Neither of these models considers the effect of cell confinement, which plays a major role in single-molecule diffusion in small-sized cells such as bacteria. For these reasons, we opted to use an empirical fit to the data. We note that the fractions of active ribosomes in WT cells, which we extracted from these diffusion measurements, are consistent with the range of estimates obtained by others using similar or different approaches (Forchhammer and Lindhal 1971; Mohapatra and Weisshaar, 2018; Sanamrad et al., 2014). 

The estimated fraction of active ribosomes in wild-type cells shows a very strong reduction with decreasing growth rate (down from 75% to 30%), twice as strong as measured in bulk experiments (Dai et al Nat Microbiology 2016; decrease from 90% to 60% for the same growth rate range) and probably incompatible with measurements of growth rate, ribosome concentrations, and almost constant translation elongation rate in this regime of growth rates. Might the different diffusive fractions of RpsB not represent active/inactive ribosomes? See also the problem of quantification above. The authors should explain and compare their results to previous work. 

We agree that our measured range is somewhat larger than the estimated range from Dai et al, 2016. However, they use different media, strains, and growth conditions. We also note that Dai et al did not make actual measurements of the active ribosome fraction. Instead, they calculate the “active ribosome equivalent” based on a model that includes growth rate, protein synthesis rate, RNA/protein abundance, and the total number of amino acids in all proteins in the cell. Importantly, our measurements show the same overall trend (a ~30% decrease) as Dai et al, 2016. Furthermore, our results are within the range of previous experimental estimates from ribosome profiling (Forchhammer and Lindhal 1971) or single-ribosome tracking (Mohapatra and Weisshaar, 2018; Sanamrad et al., 2014). We clarified this point in the revised manuscript. 

To measure the reduction of mRNA transcripts in the cell, the authors rely on the fluorescent dye SYTO RNAselect. They argue that 70% of the dye signal represents mRNA. The argument is based on the previously observed reduction of the total signal by 70% upon treatment with rifampicin, an RNA polymerase inhibitor (Bakshi et al 2014). The idea here is presumably that mRNA should undergo rapid degradation upon rif treatment while rRNA or tRNA are stable. However, work from Hamouche et al. RNA (2021) 27:946 demonstrates that rifampicin treatment also leads to a rapid degradation of rRNA. Furthermore, the timescale of fluorescent-signal decay in the paper by Bakshi et al. (half life about 10min) is not compatible with the previously reported rapid decay of mRNA (24min) but rather compatible with the slower, still somewhat rapid, decay of rRNA reported by Hamouche et al.. A bulk method to measure total mRNA as in the cited Balakrishnan et al. (Science 2022) would thus be a preferred method to quantify mRNA. Alternatively, the authors could also test whether the mass contribution of total RNA remains constant, which would suggest that rRNA decay does not contribute to signal loss. However, since rRNA dominates total RNA, this measurement requires high accuracy. The authors might thus tone down their conclusions on mRNA concentration changes while still highlighting the compelling data on RNAp diffusion. 

Thank you for bringing the Hamouche et al 2021 paper to our attention. To address this potential issue, we have performed fluorescence in situ hybridization (FISH) microscopy using a 16S rRNA probe (EUB338) to quantify rRNA concentration in 1N cells. We found that the rRNA signal only slightly decreases with cell size (i.e., genome dilution) compared to the RNASelect signal (e.g., a ~5% decrease for rRNA signal vs. 50% for RNASelect for a cell size range of 4 to 10 µm2). We have revised the text and added a figure to include the new rRNA FISH data (Figure 4). In addition, as a control, we validated our rRNA FISH method by comparing the intracellular concentration of 16S rRNA in poor vs. rich media (new Figure 4 – Figure supplement 3).

The proteomics experiments are a great addition to the single-cell studies, and the correlations between distance from ori and protein abundance is compelling. However, I was missing a different test, the authors might have already done but not put in the manuscript: If DNA is indeed limiting the initiation of transcription, genes that are already highly transcribed in non-perturbed conditions might saturate fastest upon replication inhibition, while genes rarely transcribed should have no problem to accommodate additional RNA polymerases. One might thus want to test, whether the (unperturbed) transcription initiation rate is a predictor of changes in protein composition. This is just a suggestion the authors may also ignore, but since it is an easy analysis, I chose to mention it here. 

We did not find any correlation when we examined the potential relation between RNA slopes and mRNA abundance (from our first CRISPRi oriC time point) or the transcription initiation rate (from Balakrishnan et al., 2022, PMID: 36480614) across genes. These new plots are presented in Figure 7 – Figure supplement 2B. In contrast, we found a small but significant correlation between RNA slopes and mRNA decay rates (from Balakrishnan et al., 2022, PMID: 36480614), specifically for genes with short mRNA lifetimes (new Figure 7F). This effect is consistent with our model prediction (Figure 5 – Figure supplement 2). 

Related to the proteomics, in l. 380 the authors write that the reduced expression close to the ori might reflect a gene-dosage compensatory mechanism. I don't understand this argument. Can the authors add a sentence to explain their hypothesis? 

We apologize for the confusion. While performing additional analyses for the revisions, we realized that while the proteins encoded by genes close to oriC tend to display subscaling behavior, this is not true at the mRNA level (new Figure 7 – Figure supplement 3B). In light of this result, we no longer have a hypothesis for the observed negative correlation at the protein level (originally Figure 5D, now Figure 7 – Figure supplement 3A). The text was revised accordingly.  

In Fig. 1E the authors show evidence that growth rate increases with cell length/area. While this is not a main point of the paper it might be cited by others in the future. There are two possible artifacts that could influence this experiment: a) segmentation: an overestimation of the physical length of the cell based on phase-contrast images (e.g., 200 nm would cause a 10% error in the relative rate of 2 um cells, but not of longer cells). b) timedependent changes of growth rate, e.g., due to change from liquid to solid or other perturbations. To test for the latter, one could measure growth rate as a function of time, restricting the analysis to short or long cells, or measuring growth rate for short/long cells at selected time points. For the former, I recommend comparison of phase-contrast segmentation with FM4-64-stained cell boundaries.

As the reviewer notes, the small increase in relative growth was just a minor observation that does not affect our story whether it is biologically meaningful or the result of a technical artefact. But we agree with the reviewer that others might cite it in future works and thus should be interpreted with caution.

An artefact associated with time-dependent changes (e.g. changing from liquid cultures to more solid agarose pads) is unlikely for two reasons. 1. We show that varying the time that cells spend on agarose pads relative to liquid cultures does not affect the cell size-dependent growth rate results (Figure 1 – supplement 5A). 2. We show that the growth rate is stable from the beginning of the time-lapse with no transient effects upon cell placement on agarose pads for imaging (Figure 1 – supplement 1). These results were described in the Methods section where they could easily be missed. We revised the text to discuss these controls more prominently in the Results section.

As for cell segmentation, we have run simulations and agree with the reviewer that a small overestimation of cell area (which is possible with any cell segmentation methods including ours) could lead to a small increase in relative growth with increasing cell areas (new Figure 1 – Figure supplement 3). Since the finding is not important to our story, we simply revised the text and added the simulation results to alert the readers to the possibility that the observation may be due to a small cell segmentation bias.

Reviewer #2 (Public Review): 

In this work, the authors uncovered the effects of DNA dilution on E. coli, including a decrease in growth rate and a significant change in proteome composition. The authors demonstrated that the decline in growth rate is due to the reduction of active ribosomes and active RNA polymerases because of the limited DNA copy numbers. They further showed that the change in the DNA-to-volume ratio leads to concentration changes in almost 60% of proteins, and these changes mainly stem from the change in the mRNA levels. 

Thank you for the support and accurate summary!

Reviewer #3 (Public Review): 

Summary: 

Mäkelä et al. here investigate genome concentration as a limiting factor on growth.

Previous work has identified key roles for transcription (RNA polymerase) and translation (ribosomes) as limiting factors on growth, which enable an exponential increase in cell mass. While a potential limiting role of genome concentration under certain conditions has been explored theoretically, Mäkelä et al. here present direct evidence that when replication is inhibited, genome concentration emerges as a limiting factor. 

Strengths: 

A major strength of this paper is the diligent and compelling combination of experiment and modeling used to address this core question. The use of origin- and ftsZ-targeted CRISPRi is a very nice approach that enables dissection of the specific effects of limiting genome dosage in the context of a growing cytoplasm. While it might be expected that genome concentration eventually becomes a limiting factor, what is surprising and novel here is that this happens very rapidly, with growth transitioning even for cells within the normal length distribution for E. coli. Fundamentally, it demonstrates the fine balance of bacterial physiology, where the concentration of the genome itself (at least under rapid growth conditions) is no higher than it needs to be. 

Thank you!

Weaknesses: 

One limitation of the study is that genome concentration is largely treated as a single commodity. While this facilitates their modeling approach, one would expect that the growth phenotypes observed arise due to copy number limitation in a relatively small number of rate-limiting genes. The authors do report shifts in the composition of both the proteome and the transcriptome in response to replication inhibition, but while they report a positional effect of distance from the replication origin (reflecting loss of high-copy, origin-proximal genes), other factors shaping compositional shifts and their functional effects on growth are not extensively explored. This is particularly true for ribosomal RNA itself, which the authors assume to grow proportionately with protein. More generally, understanding which genes exert the greatest copy number-dependent influence on growth may aid both efforts to enhance (biotechnology) and inhibit (infection) bacterial growth. 

We agree but feel that identifying the specific limiting genes is beyond the scope of the study. This said, we carried out additional experiments and analyses to address the reviewer’s comment and identify potential contributing factors and limiting gene candidates. First, we examined the intracellular concentration of 16S ribosomal RNA (rRNA) by rRNA FISH microscopy and found that it decays much slower than the bulk of mRNAs as measured using RNASelect staining (new Figure 4 and Figure 4 – Figure supplements 1 and 3). We found that the rRNA signal is far more stable in 1N cells than the RNASelect signal, the former decreasing by only ~5% versus ~50% for the later in response to the same range of genome dilution (Figure 4C).  Second,  we carried out new correlation analyses between our proteomic/transcriptomic datasets and published genome-wide datasets that report various variables under unperturbed conditions (e.g., mRNA abundance, mRNA degradation rates, fitness cost, transcription initiation rates, essentiality for viability); see new Figure 7E-G and Figure 7 – Figure supplement 2. In the process, we found that genes essential for viability tend, on average, to display superscaling behavior (Figure 7G). This suggests that cells have evolved mechanisms that prioritize expression of essential genes over nonessential ones during DNA-limited growth. Furthermore, this analysis identified a small number of essential genes that display strong negative RNA slopes (Figure 7C, Datasets 1 and 2), indicating that the concentration of their mRNA decreases rapidly relative to the rest of the transcriptome upon genome dilution. These essential genes with strong subscaling behavior are candidates for being growth-limiting. 

The text and figures were revised to include these new results.

Overall, this study provides a fundamental contribution to bacterial physiology by illuminating the relationship between DNA, mRNA, and protein in determining growth rate. While coarse-grained, the work invites exciting questions about how the composition of major cellular components is fine-tuned to a cell's needs and which specific gene products mediate this connection. This work has implications not only for biotechnology, as the authors discuss, but potentially also for our understanding of how DNA-targeted antibiotics limit bacterial growth. 

Thank you!

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors): 

Below are my comments. 

(1) I noticed that a paper by Li et al. on biorxiv has found similar results as this work ("Scaling between DNA and cell size governs bacterial growth homeostasis and resource allocation," https://doi.org/10.1101/2021.11.12.468234), including the linear growth of E. coli when the DNA concentration is low. This relevant reference was not cited or discussed in the current manuscript. 

We agree that authors should cite and discuss relevant peer-reviewed literature. But broadly speaking, we feel that extending this responsibility to all preprints (and by extension any online material) that have not been reviewed is a bit dangerous. It would effectively legitimize unreviewed claims and risk their propagation in future publications. We think that while imperfect, the peer-reviewing process still plays an important role. 

Regarding the specific 2021 preprint that the reviewer pointed out, we think that the presented growth rate data are quite noisy and that the experiments lack a critical control (multi-N cells), making interpretation difficult. Their report that plasmid-borne expression is enhanced when DNA is severely diluted is certainly interesting and makes sense in light of our measurements that the activities, but not the concentrations, of RNA polymerases and ribosomes are reduced in 1N cells. However, we do not know why this preprint has not yet been published since 2021. There could be many possible reasons for this. Therefore, we feel that it is safer to limit our discussion to peer-reviewed literature.

(2) I think the kinetic Model B in the Appendix has been studied in previous works, such as Klump & Hwa, PNAS 2008, https://doi.org/10.1073/pnas.0804953105

Indeed, Klumpp & Hwa 2008 modeled the kinetics of RNA polymerase and promoter association prior to our study. But there is a difference between their model and ours. Their model is based on Michaelis Menten-type (MM) functions in which the RNAP is analogous to the “substrate” and the promoter to the “enzyme” in the MM equation. In contrast, our model uses functions based on the law of mass action (instead of MMtype of function). We have revised the text, included the Klumpp & Hwa 2008 reference, and revised the Materials & Methods section to clarify these points. 

(3) On lines 284-285, if I understand correctly, the fractions of active RNAPs and active ribosomes are relative to the total protein number. It would be helpful if the authors could mention this explicitly to avoid confusion. 

The fractions of active RNAPs and active ribosomes are expressed as the percentage of the total RNAPs and ribosomes. We have revised the text to be more explicit. Thank you.

(4) On line 835, I am not sure what the bulk transcription/translation rate means. I guess it is the maximum transcription/translation rate if all RNAPs/ribosomes are working according to Eq. (1,2). It would be helpful if the authors could explain the meaning of r_1 and r_2 more explicitly. 

Our apology for the lack of clarity. We have added the following equations:

(5) Regarding the changes in protein concentrations due to genome dilution, a recent theoretical paper showed that it may come from the heterogeneity in promoter strengths (Wang & Lin, Nature Communications 2021). 

In the Wang and Lin model, the heterogeneity in promoter strength predicts that the “mRNA production rate equivalent”, which is the mRNA abundance multiplied by the mRNA decay rate, will correlate the RNA slopes. However, we found these two variables to be uncorrelated (see below, The Spearman correlation coefficient ρ was 0.02 with a p-value of 0.24, indicating non-significance (NS).

Author response image 1.

The mRNA production rate equivalent (mRNA abundance at the first time point after CRISPRi oriC induction multiplied by the mRNA degradation rate measured by Balakrishnan et al., 2022, PMID: 36480614, expressed in transcript counts per minute) does not correlate (Spearman correlation’s p-value = 0.24) with the RNA slope in 1N-rich cells.  Data from 2570 genes are shown (grey markers, Gaussian kernel density estimation - KDE), and their binned statistics (mean +/- SEM, ~280 genes per bin, orange markers). 

In addition, we found no significant correlation between RNA slopes and mRNA abundance or transcription initiation rate. These plots are now included in Figure 7E and Figure 7 –Figure supplement 2B. Thus, the promoter strength does not appear to be a predictor of the RNA (and protein) scaling behavior under DNA limitation. 

Reviewer #3 (Recommendations For The Authors): 

One general area that could be developed further is analysis of changes in the proteome/transcriptome composition, given that there may be specific clues here as to the phenotypic effects of genome concentration limitation. Specifically: 

• In Figure 5D, the authors demonstrate an effect of origin distance on sensitivity to replication inhibition, presumably as a copy number effect. However, the authors note that the effect was only slight and postulated a compensatory mechanism. Due to the stability of proteins, one should expect relatively small effects - even if synthesis of a protein stopped completely, its concentration would only decrease twofold with a doubling of cell area (slope = -1, if I'm interpreting things correctly). It would be helpful to display the same information shown in Figure 5D at the mRNA level, since I would anticipate that higher mRNA turnover rates mean that effects on transcription rate should be felt more rapidly. 

We thank the reviewer for this suggestion. To our surprise, we found that there is no correlation between gene location relative to the origin and RNA slope across genes. This suggests that the observed correlation between gene location and protein slopes does not occur at the mRNA level. Given that we do not have an explanation for the underlying mechanism, we decided to present these data (the original data in Figure 5D and the new data for the RNA slope) in a supplementary figure (Figure 7 – Figure supplement 3).

• Related to this, did the authors see any other general trends? For example, do highly expressed genes hit saturation faster, making them more sensitive to limited genome concentration? 

We found that the RNA slopes do not correlate with mRNA abundance or transcription initiation rates. However, they do correlate with mRNA decay. That is, short-lived mRNAs tend to have negative RNA slopes. The new analyses have been added as Figure 7E-F and Figure 7 – Figure supplement 2B. The text has been revised to incorporate this information. 

• Presumably loss of growth is primarily driven by a subset of genes whose copy number becomes limiting. Previously, it has been reported that there is a wide variety among "essential" genes in their expression-fitness relationship - i.e. how much of a reduction in expression you need before growth is reduced (e.g. PMID 33080209). It would be interesting to explore the shifts in proteome/transcriptome composition to see whether any genes particularly affected by restricted genome concentration are also especially sensitive to reduced expression - overlap in these datasets may reveal which genes drive the loss of growth. 

This is a very interesting idea – thank you! We did not find a correlation between the protein/RNA slope and the relative gene fitness as previously calculated (PMID 33080209), as shown below.

Author response image 2.

The relative fitness of each gene (data by Hawkins et al., 2020, PMID: 33080209, median fitness from the highest sgRNA activity bin) plotted versus the gene-specific RNA and protein slopes that we measured in 1Nrich cells after CRISPRi oriC induction. More than 260 essential genes are shown (262 RNA slopes and 270 protein slopes, grey markers), and their binned statistics (mean +/- SEM, 43-45 essential genes per bin, orange markers). The spearman correlations (ρ) with p-values above 10-3 are considered not significant (NS). In our analyses, we only considered correlations significant if they have a Spearman correlation p-value below 10-10.

However, while doing this suggested analysis, we noticed that the essential genes that were included in the forementioned study have RNA slopes above zero on average. This led us to compare the RNA slope distributions of essential genes relative to all genes (now included in Figure 7G). We found that they tend to display superscaling behavior (positive RNA slopes), suggesting the existence of regulatory mechanisms that prioritize the expression of essential genes over less important ones when genome concentration becomes limiting for growth.  The text has been revised to include this new information.

Other suggestions: 

• In Figure 3 the authors report that total RNAP concentration increases with increasing cytoplasmic volume. This is in itself an interesting finding as it may imply a compensatory mechanism - can the authors offer an explanation for this? 

We do not have a straightforward explanation. But we agree that it is very interesting and should be investigated in future studies given that this superscaling behavior is common among essential genes. 

• The explanation of the modeling within the main text could be improved. Specifically, equations 1 and 2, as well as a discussion of models A and B (lines 290-301), do not explicitly relate DNA concentration to downstream effects. The authors provide the key information in Appendix 1, but for a general reader, it would be helpful to provide some intuition within the main text about how genome concentration influences transcription rate (i.e. via 𝛼RNAP).  

We apologize for the lack of clarity. We have added information that hopefully improves clarity.

Author Response

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

eLife assessment

This article presents important results describing how the gathering, integration, and broadcasting of information in the brain changes when consciousness is lost either through anesthesia or injury. They provide convincing evidence to support their conclusions, although the paper relies on a single analysis tool (partial information decomposition) and could benefit from a clearer explication of its conceptual basis, methodology, and results. The work will be of interest to both neuroscientists and clinicians interested in fundamental and clinical aspects of consciousness.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, Luppi et al., apply the recently developed integrated information decomposition to the question how the architecture of information processing changes when consciousness is lost. They explore fMRI data from two different populations: healthy volunteers undergoing reversible anesthesia, as well as from patients who have long-term disorders of consciousness. They show that, in both populations, synergistic integration of information is disrupted in common ways. These results are interpreted in the context of the SAPHIRE model (recently proposed by this same group), that describes information processing in the brain as being composed of several distinct steps: 1) gatekeeping (where gateway regions introduce sensory information to the global synergistic workspace where 2) it is integrated or "processed" before 3) by broadcast back to to the brain.

I think that this paper is an excellent addition to the literature on information theory in neuroscience, and consciousness science specifically. The writing is clear, the figures are informative, and the authors do a good job of engaging with existing literature. While I do have some questions about the interpretations of the various information-theoretic measures, all in all, I think this is a significant piece of science that I am glad to see added to the literature.

One specific question I have is that I am still a little unsure about what "synergy" really is in this context. From the methods, it is defined as that part of the joint mutual information that is greater than the maximum marginal mutual information. While this is a perfectly fine mathematical measure, it is not clear to me what that means for a squishy organ like the brain. What should these results mean to a neuro-biologist or clinician?

Right now the discussion is very high level, equating synergy to "information processing" or "integrated information", but it might be helpful for readers not steeped in multivariate information theory to have some kind of toy model that gets worked out in detail. On page 15, the logical XOR is presented in the context of the single-target PID, but 1) the XOR is discrete, while the data analyzed here are continuous BOLD signals w/ Gaussian assumptions and 2) the XOR gate is a single-target system, while the power of the Phi-ID approach is the multi-target generality. Is there a Gaussian analog of the single-target XOR gate that could be presented? Or some multi-target, Gaussian toy model with enough synergy to be interesting? I think this would go a long way to making this work more accessible to the kind of interdisciplinary readership that this kind of article with inevitably attract.

We appreciate this observation. We now clarify that:

“redundancy between two units occurs when their future spontaneous evolution is predicted equally well by the past of either unit. Synergy instead occurs when considering the two units together increases the mutual information between the units’ past and their future – suggesting that the future of each is shaped by its interactions with the other. At the microscale (e.g., for spiking neurons) this phenomenon has been suggested as reflecting “information modification” 36,40,47. Synergy can also be viewed as reflecting the joint contribution of parts of the system to the whole, that is not driven by common input48.”

In the Methods, we have also added the following example to provide additional intuition about synergy in the case of continuous rather than discrete variables:

“As another example for the case of Gaussian variables (as employed here), consider a 2-node coupled autoregressive process with two parameters: a noise correlation c and a coupling parameter a. As c increases, the system is flooded by “common noise”, making the system increasingly redundant because the common noise “swamps” the signal of each node. As a increases, each node has a stronger influence both on the other and on the system as a whole, and we expect synergy to increase. Therefore, synergy reflects the joint contribution of parts of the system to the whole that is not driven by common noise. This has been demonstrated through computational modelling (Mediano et al 2019 Entropy).”

See below for the relevant parts of Figures 1 and 2 from Mediano et al (2019 Entropy), where Psi refers to the total synergy in the system.

Author response image 1.

Strengths

The authors have a very strong collection of datasets with which to explore their topic of interest. By comparing fMRI scans from patients with disorders of consciousness, healthy resting state, and various stages of propofol anesthesia, the authors have a very robust sample of the various ways consciousness can be perturbed, or lost. Consequently, it is difficult to imagine that the observed effects are merely a quirk of some biophysical effect of propofol specifically, or a particular consequence of long-term brain injury, but do in fact reflect some global property related to consciousness. The data and analyses themselves are well-described, have been previously validated, and are generally strong. I have no reason to doubt the technical validity of the presented results.

The discussion and interpretation of these results is also very nice, bringing together ideas from the two leading neurocognitive theories of consciousness (Global Workspace and Integrated Information Theory) in a way that feels natural. The SAPHIRE model seems plausible and amenable to future research. The authors discuss this in the paper, but I think that future work on less radical interventions (e.g. movie watching, cognitive tasks, etc) could be very helpful in refining the SAPHIRE approach.

Finally, the analogy between the PID terms and the information provided by each eye redundantly, uniquely, and synergistically is superb. I will definitely be referencing this intuition pump in future discussions of multivariate information sharing.

We are very grateful for these positive comments, and for the feedback on our eye metaphor.

Weaknesses

I have some concerns about the way "information processing" is used in this study. The data analyzed, fMRI BOLD data is extremely coarse, both in spatial and temporal terms. I am not sure I am convinced that this is the natural scale at which to talk about information "processing" or "integration" in the brain. In contrast to measures like sample entropy or Lempel-Ziv complexity (which just describe the statistics of BOLD activity), synergy and Phi are presented here as quasi-causal measures: as if they "cause" or "represent" phenomenological consciousness. While the theoretical arguments linking integration to consciousness are compelling, is this is right data set to explore them in? For example, the work by Newman, Beggs, and Sherril (nee Faber), synergy is associated with "computation" performed in individual neurons: the information about the future state of a target neuron that is only accessible when knowing both inputs (analogous to the synergy in computing the sum of two dice). Whether one thinks that this is a good approach neural computation or not, it fits within the commonly accepted causal model of neural spiking activity: neurons receive inputs from multiple upstream neurons, integrate those inputs and change their firing behavior accordingly.

In contrast, here, we are looking at BOLD data, which is a proxy measure for gross-scale regional neural activity, which itself is a coarse-graining of millions of individual neurons to a uni-dimensional spectrum that runs from "inactive to active." It feels as though a lot of inferences are being made from very coarse data.

We appreciate the opportunity to clarify this point. It is not our intention to claim that Phi-R and synergy, as measured at the level of regional BOLD signals, represent a direct cause of consciousness, or are identical to it. Rather, our work is intended to use these measures similarly to the use of sample entropy and LZC for BOLD signals: as theoretically grounded macroscale indicators, whose empirical relationship to consciousness may reveal the relevant underlying phenomena. In other words, while our results do show that BOLD-derived Phi-R tracks the loss and recovery of consciousness, we do not claim that they are the cause of it: only that an empirical relationship exists, which is in line with what we might expect on theoretical grounds. We have now clarified this in the Limitations section of our revised manuscript, as well as revising our language accordingly in the rest of the manuscript.

We also clarify that the meaning of “information processing” that we adopt pertains to “intrinsic” information that is present in the system’s spontaneous dynamics, rather than extrinsic information about a task:

“Information decomposition can be applied to neural data from different scales, from electrophysiology to functional MRI, with or without reference to behaviour 34. When behavioural data are taken into account, information decomposition can shed light on the processing of “extrinsic” information, understood as the translation of sensory signals into behavioural choices across neurons or regions 41,43,45,47. However, information decomposition can also be applied to investigate the “intrinsic” information that is present in the brain’s spontaneous dynamics in the absence of any tasks, in the same vein as resting-state “functional connectivity” and methods from statistical causal inference such as Granger causality 49. In this context, information processing should be understood in terms of the dynamics of information: where and how information is stored, transferred, and modified 34.”

References:

(1) Newman, E. L., Varley, T. F., Parakkattu, V. K., Sherrill, S. P. & Beggs, J. M. Revealing the Dynamics of Neural Information Processing with Multivariate Information Decomposition. Entropy 24, 930 (2022).

Reviewer #2 (Public Review):

The authors analysed functional MRI recordings of brain activity at rest, using state-of-the-art methods that reveal the diverse ways in which the information can be integrated in the brain. In this way, they found brain areas that act as (synergistic) gateways for the 'global workspace', where conscious access to information or cognition would occur, and brain areas that serve as (redundant) broadcasters from the global workspace to the rest of the brain. The results are compelling and consisting with the already assumed role of several networks and areas within the Global Neuronal Workspace framework. Thus, in a way, this work comes to stress the role of synergy and redundancy as complementary information processing modes, which fulfill different roles in the big context of information integration.

In addition, to prove that the identified high-order interactions are relevant to the phenomenon of consciousness, the same analysis was performed in subjects under anesthesia or with disorders of consciousness (DOC), showing that indeed the loss of consciousness is associated with a deficient integration of information within the gateway regions.

However, there is something confusing in the redundancy and synergy matrices shown in Figure 2. These are pair-wise matrices, where the PID was applied to identify high-order interactions between pairs of brain regions. I understand that synergy and redundancy are assessed in the way the brain areas integrate information in time, but it is still a little contradictory to speak about high-order in pairs of areas. When talking about a "synergistic core", one expects that all or most of the areas belonging to that core are simultaneously involved in some (synergistic) information processing, and I do not see this being assessed with the currently presented methodology. Similarly, if redundancy is assessed only in pairs of areas, it may be due to simple correlations between them, so it is not a high-order interaction. Perhaps it is a matter of language, or about the expectations that the word 'synergy' evokes, so a clarification about this issue is needed. Moreover, as the rest of the work is based on these 'pair-wise' redundancy and synergy matrices, it becomes a significative issue.

We are grateful for the opportunity to clarify this point. We should highlight that PhiID is in fact assessing four variables: the past of region X, the past of region B, the future of region X, and the future of region Y. Since X and Y each feature both in the past and in the future, we can re-conceptualise the PhiID outputs as reflecting the temporal evolution of how X and Y jointly convey information: the persistent redundancy that we consider corresponds to information that is always present in both X and Y; whereas the persistent synergy is information that X and Y always convey synergistically. In contrast, information transfer would correspond to the phenomenon whereby information was conveyed by one variable in the past, and by the other in the future (see Luppi et al., 2024 TICS; and Mediano et al., 2021 arXiv for more thorough discussions on this point). We have now added this clarification in our Introduction and Results, as well as adding the new Figure 2 to clarify the meaning of PhiID terms.

We would also like to clarify that all the edges that we identify as significantly changing are indeed simultaneously involved in the difference between consciousness and unconsciousness. This is because the Network-Based Statistic differs from other ways of identifying edges that are significantly different between two groups or conditions, because it does not consider edges in isolation, but only as part of a single connected component.

Reviewer #3 (Public Review):

The work proposes a model of neural information processing based on a 'synergistic global workspace,' which processes information in three principal steps: a gatekeeping step (information gathering), an information integration step, and finally, a broadcasting step. The authors determined the synergistic global workspace based on previous work and extended the role of its elements using 100 fMRI recordings of the resting state of healthy participants of the HCP. The authors then applied network analysis and two different measures of information integration to examine changes in reduced states of consciousness (such as anesthesia and after-coma disorders of consciousness). They provided an interpretation of the results in terms of the proposed model of brain information processing, which could be helpful to be implemented in other states of consciousness and related to perturbative approaches. Overall, I found the manuscript to be well-organized, and the results are interesting and could be informative for a broad range of literature, suggesting interesting new ideas for the field to explore. However, there are some points that the authors could clarify to strengthen the paper. Key points include:

(1) The work strongly relies on the identification of the regions belonging to the synergistic global workspace, which was primarily proposed and computed in a previous paper by the authors. It would be great if this computation could be included in a more explicit way in this manuscript to make it self-contained. Maybe include some table or figure being explicit in the Gradient of redundancy-to-synergy relative importance results and procedure.

We have now added the new Supplementary Figure 1 to clarify how the synergistic workspace is identified, as per Luppi et al (2022 Nature Neuroscience).

(2) It would be beneficial if the authors could provide further explanation regarding the differences in the procedure for selecting the workspace and its role within the proposed architecture. For instance, why does one case uses the strength of the nodes while the other case uses the participation coefficient? It would be interesting to explore what would happen if the workspace was defined directly using the participation coefficient instead of the strength. Additionally, what impact would it have on the procedure if a different selection of modules was used? For example, instead of using the RSN, other criteria, such as modularity algorithms, PCA, Hidden Markov Models, Variational Autoencoders, etc., could be considered. The main point of my question is that, probably, the RSN are quite redundant networks and other methods, as PCA generates independent networks. It would be helpful if the authors could offer some comments on their intuition regarding these points without necessarily requiring additional computations.

We appreciate the opportunity to clarify this point. Our rationale for the procedure used to identify the workspace is to find regions where synergy is especially prominent. This is due to the close mathematical relationship between synergistic information and integration of information (see also Luppi et al., 2024 TICS), which we view as the core function of the global workspace. This identification is based on the strength ranking, as per Luppi et al (2022 Nature Neuroscience), which demonstrated that regions where synergy predominates (i.e., our proposed workspace) are also involved with high-level cognitive functions and anatomically coincide with transmodal association cortices at the confluence of multiple information streams. This is what we should expect of a global workspace, which is why we use the strength of synergistic interactions to identify it, rather than the participation coefficient. Subsequently, to discern broadcasters from gateways within the synergistic workspace, we seek to encapsulate the meaning of a “broadcaster” in information terms. We argue that this corresponds with making the same information available to multiple modules. Sameness of information corresponds to redundancy, and multiplicity of modules can be reflected in the network-theoretic notion of participation coefficient. Thus, a broadcaster is a region in the synergistic workspace (i.e., a region with strong synergistic interactions) that in addition has a high participation coefficient for its redundant interactions.

Pertaining specifically to the use of resting-state networks as modules, indeed our own (Luppi et al., 2022 Nature Neuroscience) and others’ research has shown that each RSN entertains primarily redundant interactions among its constituent regions. This is not surprising, since RSNs are functionally defined: their constituent elements need to process the same information (e.g., pertaining to a visual task in case of the visual network). We used the RSNs as our definition of modules, because they are widely understood to reflect the intrinsic organisation of brain activity into functional units; for example, Smith et al., (2009 PNAS) and Cole et al (2014 Neuron) both showed that RSNs reflect task-related co-activation of regions, whether directly quantified from fMRI in individuals performing multiple tasks, or inferred from meta-analysis of the neuroimaging literature. This is the aspect of a “module” that matters from the global workspace perspective: modules are units with distinct function, and RSNs capture this well. This is therefore why we use the RSNs as modules when defining the participation coefficient: they provide an a-priori division into units with functionally distinct roles.

Nonetheless, we also note that RSN organisation is robustly recovered using many different methods, including seed-based correlation from specific regions-of-interest, or Independent Components Analysis, or community detection on the network of inter-regional correlations - demonstrating that they are not merely a function of the specific method used to identify them. In fact, we show significant correlation between participation coefficient defined in terms of RSNs, and in terms of modules identified in a purely data-driven manner from Louvain consensus clustering (Figure S4).

(3) The authors acknowledged the potential relevance of perturbative approaches in terms of PCI and quantification of consciousness. It would be valuable if the authors could also discuss perturbative approaches in relation to inducing transitions between brain states. In other words, since the authors investigate disorders of consciousness where interventions could provide insights into treatment, as suggested by computational and experimental works, it would be interesting to explore the relationship between the synergistic workspace and its modifications from this perspective as well.

We thank the Reviewer for bringing this up: we now cite several studies that in recent years have applied perturbative approaches to induce transitions between states of consciousness.

“The PCI is used as a means of assessing the brain’s current state, but stimulation protocols can also be adopted to directly induce transitions between states of consciousness. In rodents, carbachol administration to frontal cortex awakens rats from sevoflurane anaesthesia120, and optogenetic stimulation was used to identify a role of central thalamus neurons in controlling transitions between states of responsiveness121,122. Additionally, several studies in non-human primates have now shown that electrical stimulation of the central thalamus can reliably induce awakening from anaesthesia, accompanied by the reversal of electrophysiological and fMRI markers of anaesthesia 123–128. Finally, in human patients suffering from disorders of consciousness, stimulation of intra-laminar central thalamic nuclei was reported to induce behavioural improvement 129, and ultrasonic stimulation 130,131 and deep-brain stimulation are among potential therapies being considered for DOC patients 132,133. It will be of considerable interest to determine whether our corrected measure of integrated information and topography of the synergistic workspace also restored by these causal interventions.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I would appreciate it if the authors could revisit the figures and make sure that:

(1) All fonts are large enough to be readable for people with visual impairments (for ex. the ranges on the colorbars in Fig. 2 are unreadably small).

Thank you: we have increased font sizes.

(2) The colormaps are scaled to show meaningful differences (Fig. 2A)

We have changed the color scale in Figure 2A and 2B.

Also, the authors may want to revisit the references section: some of the papers that were pre-prints at one point have now been published and should be updated.

Thank you: we have updated our references.

Minor comments:

• In Eqs. 2 and 3, the unique information term uses the bar notation ( | ) that is typically indicative of "conditioned on." Perhaps the authors could use a slash notation (e.g. Unq(X ; Z / Y)) to avoid this ambiguity? My understanding of the Unique information is that it is not necessarily "conditioned on", so much as it is "in the context of".

Indeed, the “|” sign of “conditioning” could be misleading; however, the “/” sign could also be misleading, if interpreted as division. Therefore, we have opted for the “\” sign of “set difference”, in Eq 2 and 3, which is conceptually more appropriate in this context.

• The font on the figures is a little bit small - for readers with poor eyes, it might be helpful to increase the wording size.

We have increased font sizes in the figures where relevant.

• I don't quite understand what is happening in Fig. 2A - perhaps it is a colormap issue, but it seems as though it's just a bit white square? It looks like redundancy is broadly correlated with FC (just based on the look of the adjacency matrices), but I have no real sense of what the synergistic matrix looks like, other than "flat."

We have now changed the color scale in Figure 2.

Reviewer #2 (Recommendations For The Authors):

Besides the issues mentioned in the Public review, I have the following suggestions to improve the manuscript:

• At the end of the introduction, a few lines could be added explaining why the study of DOC patients and subjects under anesthesia will be informative in the context of this work.

By comparing functional brain scans from transient anaesthetic-induced unconsciousness and from the persistent unconsciousness of DOC patients, which arises from brain injury, we can search for common brain changes associated with loss of consciousness – thereby disambiguating what is specific to loss of consciousness.

• On page and in general the first part of Results, it is not evident that you are working with functional connectivity. Many times the word 'connection' is used and sometimes I was wondering whether they were structural or functional. Please clarify. Also, the meaning of 'synergistic connection' or 'redundant connection' could be explained in lay terms.

Thank you for bringing this up. We have now replaced the word “connection” with “interaction” to disambiguate this issue, further adding “functional” where appropriate. We have also provided, in the Introduction, an intuitive explanation of what synergy and redundancy mean int he context of spontaneous fMRI signals.

• Figure 2 needs a lot of improvement. The matrix of synergistic interactions looks completely yellow-ish with some vague areas of white. So everything is above 2. What does it mean?? Pretty uninformative. The matrix of redundant connections looks a lot of black, with some red here and there. So everything is below 0.6. Also, what are the meaning and units of the colorbars?.

We agree: we have increased font sizes, added labels, and changed the color scale in Figure 2. We hope that the new version of Figure 2 will be clearer.

• Caption of Figure 2 mentions "... brain regions identified as belonging to the synergistic global workspace". I didn't get it clear how do you define these areas. Are they just the sum of gateways and broadcasters, or is there another criterion?

Regions belonging to the synergistic workspace are indeed the set comprising gateways and broadcasters; they are the regions that are synergy-dominated, as defined in Luppi et al., 2022 Nature Neuroscience. We have now clarified this in the figure caption.

• In the first lines of page 7, it is said that data from DOC and anesthesia was parcellated in 400 + 54 regions. However, it was said in a manner that made me think it was a different parcellation than the other data. Please make it clear that the parcellation is the same (if it is).

We have now clarified that the 400 cortical regions are from the Schaefer atlas, and 54 subcortical regions from the Tian atlas, as for the other analysis. The only other parcellation that we use is the Schaefer-232, for the robustness analysis. This is also reported in the Methods.

• Figure 3: the labels in the colorbars cannot be read, please make them bigger. Also, the colorbars and colorscales should be centered in white, to make it clear that red is positive and blue is negative. O at least maintain consistency across the panels (I can't tell because of the small numbers).

Thank you: we have increased font sizes, added labels, indicated that white refers to zero (so that red is always an increase, and blue is always a decrease), and changed the color scale in Figure 2.

• The legend of Figure 4 is written in a different style, interpreting the figure rather than describing it. Please describe the figure in the caption, in order to let the read know what they are looking at.

We have endeavoured to rewrite the legend of Figure 4 in a style that is more consistent with the other figures.

• In several parts the 'whole-minus-sum' phi measure is mentioned and it is said that it did not decrease during loss of consciousness. However, I did not see any figure about that nor any conspicuous reference to that in Results text. Where is it?

We apologise for the confusion: this is Figure S3A, in the Supplementary. We have now clarified this in the text.

Reviewer #3 (Recommendations For The Authors):

(1) In the same direction, regarding Fig. 2, in my opinion, it does not effectively aid in understanding the selection of regions as more synergistic or redundant. In panels A) and B), the color scales could be improved to better distinguish regions in the matrices (panel A) is saturated at the upper limit, while panel B) is saturated at the lower limit). Additionally, I suggest indicating in the panels what is being measured with the color scales.

Thank you: we have increased font sizes, added labels, and changed the color scale in Figure 2.

(2) When investigating the synergistic core of human consciousness and interpreting the results of changes in information integration measures in terms of the proposed framework, did the authors consider the synergistic workspace computed in HCP data? If the answer is positive, it would be helpful for the authors to be more explicit about it and elaborate on any differences that may be found, as well as the potential impact on interpretation.

This is correct: the synergistic workspace, including gateways and broadcasters, are identified from the Human Connectome Project dataset. We now clarify this in the manuscript.

Minors:

(1) I would suggest improving the readability of figures 2 and 3, considering font size (letters and numbers) and color bars (numbers and indicate what is measured with this scale). In Figure 1, the caption defines steps instead stages that are indicated in the figure.

Thank you: we have increased font sizes, added labels, and replaced steps with “stages” in Figure 1.

Author response:

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

We summarized the main changes:

(1) In the Introduction part, we give a general definition of habitat fragmentation to avoid confusion, as reviewers #1 and #2 suggested.

(2) We clarify the two aspects of the observed “extinction”——“true dieback” and “emigration”, as reviewers #2 and #3 suggested.

(3) In the Methods part, we 1) clarify the reason for testing the temporal trend in colonization/extinction dynamics and describe how to select islands as reviewer #1 suggested; 2) describe how to exclude birds from the analysis as reviewer #2 suggested.

(4) In the Results part, we modified and rearranged Figure 4-6 as reviewers #1, #2 and #3 suggested.

(5) In the Discussion part, we 1) discuss the multiple aspects of the metric of isolation for future research as reviewer #3 suggested; 2) provide concrete evidence about the relationship between habitat diversity or heterogeneity and island area and 3) provide a wider perspective about how our results can inform conservation practices in fragmented habitats as reviewer #2 suggested.

eLife Assessment

This important study enhances our understanding of how habitat fragmentation and climate change jointly influence bird community thermophilization in a fragmented island system. The evidence supporting some conclusions is incomplete, as while the overall trends are convincing, some methodological aspects, particularly the isolation metrics and interpretation of colonization/extinction rates, require further clarification. This work will be of broad interest to ecologists and conservation biologists, providing crucial insights into how ecosystems and communities react to climate change.

We sincerely extend our gratitude to you and the esteemed reviewers for acknowledging the importance of our study and for raising these concerns. We have clarified the rationale behind our analysis of temporal trends in colonization and extinction dynamics, as well as the choice of distance to the mainland as the isolation metric. Additionally, we further discuss the multiple aspects of the metric of isolation for future research and provide concrete supporting evidence about the relationship between habitat diversity or heterogeneity and island area.

Incorporating these valuable suggestions, we have thoroughly revised our manuscript, ensuring that it now presents a more comprehensive and nuanced account of our research. We are confident that these improvements will further enhance the impact and relevance of our work for ecologists and conservation biologists alike, offering vital insights into the resilience and adaptation strategies of communities facing the challenges of climate change.

Reviewer #1 (Public Review):

Summary:

This study reports on the thermophilization of bird communities in a network of islands with varying areas and isolation in China. Using data from 10 years of transect surveys, the authors show that warm-adapted species tend to gradually replace cold-adapted species, both in terms of abundance and occurrence. The observed trends in colonisations and extinctions are related to the respective area and isolation of islands, showing an effect of fragmentation on the process of thermophilization.

Strengths:

Although thermophilization of bird communities has been already reported in different contexts, it is rare that this process can be related to habitat fragmentation, despite the fact that it has been hypothesized for a long time that it could play an important role. This is made possible thanks to a really nice study system in which the construction of a dam has created this incredible Thousand Islands lake. Here, authors do not simply take observed presence-absence as granted and instead develop an ambitious hierarchical dynamic multi-species occupancy model. Moreover, they carefully interpret their results in light of their knowledge of the ecology of the species involved.

Response: We greatly appreciate your recognition of our study system and the comprehensive approach and careful interpretation of results. 

Weaknesses:

Despite the clarity of this paper on many aspects, I see a strong weakness in the authors' hypotheses, which obscures the interpretation of their results. Looking at Figure 1, and in many sentences of the text, a strong baseline hypothesis is that thermophilization occurs because of an increasing colonisation rate of warm-adapted species and extinction rate of cold-adapted species. However, there does not need to be a temporal trend! Any warm-adapted species that colonizes a site has a positive net effect on CTI; similarly, any cold-adapted species that goes extinct contributes to thermophilization.

Thank you very much for these thoughtful comments. The understanding depends on the time frame of the study and specifically, whether the system is at equilibrium. We think your claim is based on this background: if the system is not at equilibrium, then CTI can shift simply by having differential colonization (or extinction) rates for warm-adapted versus cold-adapted species. We agree with you in this case.

On the other hand, if a community is at equilibrium, then there will be no net change in CTI over time. Imagine we have an archipelago where the average colonization of warm-adapted species is larger than the average colonization of cold-adapted species, then over time the archipelago will reach an equilibrium with stable colonization/extinction dynamics where the average CTI is stable over time. Once it is stable, then if there is a temporal trend in colonization rates, the CTI will change until a new equilibrium is reached (if it is reached).

For our system, the question then is whether we can assume that the system is or has ever been at equilibrium. If it is not at equilibrium, then CTI can shift simply by having differential colonization (or extinction) rates for warm-adapted versus cold-adapted species. If the system is at equilibrium (at the beginning of the study), then CTI will only shift if there is a temporal change or trend in colonization or extinction rates.

Habitat fragmentation can affect biomes for decades after dam formation. The “Relaxation effect” (Gonzalez, 2000) refers to the fact that the continent acts as a potential species pool for island communities. Under relaxation, some species will be filtered out over time, mainly through the selective extinction of species that are highly sensitive to fragmentation. Meanwhile, for a 100-hectare patch, it takes about ten years to lose 50% of bird species; The smaller the patch area, the shorter the time required (Ferraz et al., 2003; Haddad et al., 2015). This study was conducted 50 to 60 years after the formation of the TIL, making the system with a high probability of reaching “equilibrium” through “Relaxation effect”(Si et al., 2014). We have no way of knowing exactly whether “equilibrium” is true in our system. Thus, changing rates of colonization-extinction over time is actually a much stronger test of thermophilization, which makes our inference more robust.

We add a note to the legend of Figure 1 on Lines 781-786:

“CTI can also change simply due to differential colonization-extinction rates by thermal affinity if the system is not at equilibrium prior to the study. In our study system, we have no way of knowing whether our island system was at equilibrium at onset of the study, thus, focusing on changing rates of colonization-extinction over time presents a much stronger tests of thermophilization.”

We hope this statement can make it clear. Thank you again for this meaningful question.

Another potential weakness is that fragmentation is not clearly defined. Generally, fragmentation sensu lato involves both loss of habitat area and changes in the spatial structure of habitats (i.e. fragmentation per se). Here, both area and isolation are considered, which may be slightly confusing for the readers if not properly defined.

Thank you for reminding us of that. Habitat fragmentation in this study involves both habitat loss and fragmentation per se. We have clarified the general definition in the Introduction on Lines 61-63:

“Habitat fragmentation, usually defined as the shifts of continuous habitat into spatially isolated and small patches (Fahrig, 2003), in particular, has been hypothesized to have interactive effects with climate change on community dynamics.”

Reviewer #2 (Public Review):

Summary:

This study addresses whether bird community reassembly in time is related to climate change by modelling a widely used metric, the community temperature index (CTI). The authors first computed the temperature index of 60 breeding bird species thanks to distribution atlases and climatic maps, thus obtaining a measure of the species realized thermal niche.

These indices were aggregated at the community level, using 53 survey transects of 36 islands (repeated for 10 years) of the Thousand Islands Lake, eastern China. Any increment of this CTI (i.e. thermophilization) can thus be interpreted as a community reassembly caused by a change in climate conditions (given no confounding correlations).

The authors show thanks to a mix of Bayesian and frequentist mixed effect models to study an increment of CTI at the island level, driven by both extinction (or emigration) of cold-adapted species and colonization of newly adapted warm-adapted species. Less isolated islands displayed higher colonization and extinction rates, confirming that dispersal constraints (created by habitat fragmentation per se) on colonization and emigration are the main determinants of thermophilization. The authors also had the opportunity to test for habitat amount (here island size). They show that the lack of microclimatic buffering resulting from less forest amount (a claim backed by understory temperature data) exacerbated the rates of cold-adapted species extinction while fostering the establishment of warm-adapted species.

Overall these findings are important to range studies as they reveal the local change in affinity to the climate of species comprising communities while showing that the habitat fragmentation VS amount distinction is relevant when studying thermophilization. As is, the manuscript lacks a wider perspective about how these results can be fed into conservation biology, but would greatly benefit from it. Indeed, this study shows that in a fragmented reserve context, habitat amount is very important in explaining trends of loss of cold-adapted species, hinting that it may be strategic to prioritize large habitats to conserve such species. Areas of diverse size may act as stepping stones for species shifting range due to climate change, with small islands fostering the establishment of newly adapted warm-adapted species while large islands act as refugia for cold-adapted species. This study also shows that the removal of dispersal constraints with low isolation may help species relocate to the best suitable microclimate in a heterogenous reserve context.

Thank you very much for your valuable feedback. We greatly appreciate your recognition of the scientific question to the extensive dataset and diverse approach. In particular, you provided constructive suggestions and examples on how to extend the results to conservation guidance. This is something we can’t ignore in the manuscript. We have added a paragraph to the end of the Discussion, stating how our results can inform conservation, on Lines 339-347:

‘Overall, our findings have important implications for conservation practices. Firstly, we confirmed the role of isolation in limiting range shifting. Better connected landscapes should be developed to remove dispersal constraints and facilitate species’ relocation to the best suitable microclimate. Second, small patches can foster the establishment of newly adapted warm-adapted species while large patches can act as refugia for cold-adapted species. Therefore, preserving patches of diverse sizes can act as stepping stones or shelters in a warming climate depending on the thermal affinity of species. These insights are important supplement to the previous emphasis on the role of habitat diversity in fostering (Richard et al., 2021) or reducing (Gaüzère et al., 2017) community-level climate debt.’

Strength:

The strength of the study lies in its impressive dataset of bird resurveys, that cover 10 years of continued warming (as evidenced by weather data), 60 species in 36 islands of varying size and isolation, perfect for disentangling habitat fragmentation and habitat amount effects on communities. This distinction allows us to test very different processes mediating thermophilization; island area, linked to microclimatic buffering, explained rates for a variety of species. Dispersal constraints due to fragmentation were harder to detect but confirms that fragmentation does slow down thermophilization processes.

This study is a very good example of how the expected range shift at the biome scale of the species materializes in small fragmented regions. Specifically, the regional dynamics the authors show are analogous to what processes are expected at the trailing and colonizing edge of a shifting range: warmer and more connected places display the fastest turnover rates of community reassembly. The authors also successfully estimated extinction and colonization rates, allowing a more mechanistic understanding of CTI increment, being the product of two processes.

The authors showed that regional diversity and CTI computed only by occurrences do not respond in 10 years of warming, but that finer metrics (abundance-based, or individual islands considered) do respond. This highlights the need to consider a variety of case-specific metrics to address local or regional trends. Figure Appendix 2 is a much-appreciated visualization of the effect of different data sources on Species thermal Index (STI) calculation.

The methods are long and diverse, but they are documented enough so that an experienced user with the use of the provided R script can follow and reproduce them.

Thank you very much for your profound Public Review. We greatly appreciate your recognition of the scientific question, the extensive dataset and the diverse approach. 

Weaknesses:

While the overall message of the paper is supported by data, the claims are not uniformly backed by the analysis. The trends of island-specific thermophilization are very credible (Figure 3), however, the variable nature of bird observations (partly compensated by an impressive number of resurveys) propagate a lot of errors in the estimation of species-specific trends in occupancy, abundance change, and the extinction and colonization rates. This materializes into a weak relationship between STI and their respective occupancy and abundance change trends (Figure 4a, Figure 5, respectively), showing that species do not uniformly contribute to the trend observed in Figure 3. This is further shown by the results presented in Figure 6, which present in my opinion the topical finding of the study. While a lot of species rates response to island areas are significant, the isolation effect on colonization and extinction rates can only be interpreted as a trend as only a few species have a significant effect. The actual effect on the occupancy change rates of species is hard to grasp, and this trend has a potentially low magnitude (see below).

Thank you very much for pointing out this shortcoming. The R2 between STI and their respective occupancy trends is relatively small (R2\=0.035). But the R2 between STI and their respective abundance change trends are relatively bigger, in the context of Ecology research (R2\=0.123). The R2 between STI and their respective colonization rate (R2\=0.083) and extinction rate trends (R2\=0.053) are also relatively small. Low R2 indicates that we can’t make predictions using the current model, we must notice that except STI, other factors may influence the species-specific occupancy trend. Nonetheless, it is important to notice that the standardized coefficient estimates are not minor and the trend is also significant, indicating the species-specific response is as least related to STI.

The number of species that have significant interaction terms for isolation (Figure 6) is indeed low. Although there is uncertainty in the estimation of relationships, there are also consistent trends in response to habitat fragmentation of colonization of warm-adapted species and extinction of cold-adapted species. This is especially true for the effect of isolation, where on islands nearer to the mainland, warm-adapted species (15 out of 15 investigated species) increased their colonization probability at a higher rate over time, while most cold-adapted species (21 out of 23 species) increased their extinction probability at a higher rate. We now better highlight these results in the Results and Discussion.

While being well documented, the myriad of statistical methods used by the authors ampere the interpretation of the figure as the posterior mean presented in Figure 4b and Figure 6 needs to be transformed again by a logit-1 and fed into the equation of the respective model to make sense of. I suggest a rewording of the caption to limit its dependence on the method section for interpretation.

Thank you for this suggestion. The value on the Y axis indicates the posterior mean of each variable (year, area, isolation and their interaction effects) extracted from the MSOM model, where the logit(extinction rate) or logit(colonization rate) was the response variable. All variables were standardized before analysis to make them comparable so interpretation is actually quite straight forward: positive values indicate positive influence while negative values indicate negative influence. Because the goal of Figure 6 is to display the negative/positive effect, we didn’t back-transform them. Following your advice, we thus modified the caption of Figure 6 (now renumbered as Figure 5, following a comment from Reviewer #3, to move Figure 5 to Figure 4c). The modified title and legends of Figure 5 are on Lines 817-820:

“Figure 5. Posterior estimates of logit-scale parameters related to cold-adapted species’ extinction rates and warm-adapted species’ colonization rates. Points are species-specific posterior means on the logit-scale, where parameters >0 indicate positive effects (on extinction [a] or colonization [b]) and parameters <0 indicate negative effects...”

By using a broad estimate of the realized thermal niche, a common weakness of thermophilization studies is the inability to capture local adaptation in species' physiological or behavioral response to a rise in temperature. The authors however acknowledge this limitation and provide specific examples of how species ought to evade high temperatures in this study region.

We appreciate your recognition. This is a common problem in STI studies. We hope in future studies, researchers can take more details about microclimate of species’ true habitat across regions into consideration when calculating STI. Although challenging, focusing on a smaller portion of its distribution range may facilitate achievement.

Reviewer #3 (Public Review):

Summary:

Juan Liu et al. investigated the interplay between habitat fragmentation and climate-driven thermophilization in birds in an island system in China. They used extensive bird monitoring data (9 surveys per year per island) across 36 islands of varying size and isolation from the mainland covering 10 years. The authors use extensive modeling frameworks to test a general increase in the occurrence and abundance of warm-dwelling species and vice versa for cold-dwelling species using the widely used Community Temperature Index (CTI), as well as the relationship between island fragmentation in terms of island area and isolation from the mainland on extinction and colonization rates of cold- and warm-adapted species. They found that indeed there was thermophilization happening during the last 10 years, which was more pronounced for the CTI based on abundances and less clearly for the occurrence-based metric. Generally, the authors show that this is driven by an increased colonization rate of warm-dwelling and an increased extinction rate of cold-dwelling species. Interestingly, they unravel some of the mechanisms behind this dynamic by showing that warm-adapted species increased while cold-dwelling decreased more strongly on smaller islands, which is - according to the authors - due to lowered thermal buffering on smaller islands (which was supported by air temperature monitoring done during the study period on small and large islands). They argue, that the increased extinction rate of cold-adapted species could also be due to lowered habitat heterogeneity on smaller islands. With regards to island isolation, they show that also both thermophilization processes (increase of warm and decrease of cold-adapted species) were stronger on islands closer to the mainland, due to closer sources to species populations of either group on the mainland as compared to limited dispersal (i.e. range shift potential) in more isolated islands.

The conclusions drawn in this study are sound, and mostly well supported by the results. Only a few aspects leave open questions and could quite likely be further supported by the authors themselves thanks to their apparent extensive understanding of the study system.

Strengths:

The study questions and hypotheses are very well aligned with the methods used, ranging from field surveys to extensive modeling frameworks, as well as with the conclusions drawn from the results. The study addresses a complex question on the interplay between habitat fragmentation and climate-driven thermophilization which can naturally be affected by a multitude of additional factors than the ones included here. Nevertheless, the authors use a well-balanced method of simplifying this to the most important factors in question (CTI change, extinction, and colonization, together with habitat fragmentation metrics of isolation and island area). The interpretation of the results presents interesting mechanisms without being too bold on their findings and by providing important links to the existing literature as well as to additional data and analyses presented in the appendix.

We appreciate very much for your positive and constructive comments and suggestions. Thank you for your recognition of the scientific question, the modeling approach and the conclusions. 

Weaknesses:

The metric of island isolation based on the distance to the mainland seems a bit too oversimplified as in real life the study system rather represents an island network where the islands of different sizes are in varying distances to each other, such that smaller islands can potentially draw from the species pools from near-by larger islands too - rather than just from the mainland. Thus a more holistic network metric of isolation could have been applied or at least discussed for future research. The fact, that the authors did find a signal of island isolation does support their method, but the variation in responses to this metric could hint at a more complex pattern going on in real-life than was assumed for this study.

Thank you for this meaningful question. Isolation can be measured in different ways in the study region. We chose the distance to the mainland as a measure of isolation based on the results of a previous study. One study in our system provided evidence that the colonization rate and extinction rate of breeding bird species were best fitted using distance to the nearest mainland over other distance-based measures (distance to the nearest landmass, distance to the nearest bigger landmass)(Si et al., 2014). Besides, their results produced almost identical patterns of the relationship between isolation and colonization/extinction rate (Si et al., 2014). That’s why we only selected “Distance to the mainland” in our current analysis and we do find some consistent patterns as expected. The plants on all islands were cleared out about 60 years ago due to dam construction, with all bird species coming from the mainland as the original species pool through a process called “relaxation”. This could be the reason why distance to the nearest mainland is the best predictor.

We agree with you that it’s still necessary to consider more aspects of “isolation” at least in discussion for future research. In our Discussion, we address these on Lines 292-299:

“As a caveat, we only consider the distance to the nearest mainland as a measure of fragmentation, consistent with previous work in this system (Si et al., 2014), but we acknowledge that other distance-based metrics of isolation that incorporate inter-island connections could reveal additional insights on fragmentation effects. The spatial arrangement of islands, like the arrangement of habitat, can influence niche tracking of species (Fourcade et al., 2021). Future studies should take these metrics into account to thoroughly understand the influence of isolation and spatial arrangement of patches in mediating the effect of climate warming on species.”

Further, the link between larger areas and higher habitat diversity or heterogeneity could be presented by providing evidence for this relationship. The authors do make a reference to a paper done in the same study system, but a more thorough presentation of it would strengthen this assumption further.

Thank you very much for this question. We now add more details about the relationship between habitat diversity and heterogeneity based on a related study in the same system. The observed number of species significantly increased with increasing island area (slope = 4.42, R2 = 0.70, p < .001), as did the rarefied species richness per island (slope = 1.03, R2 = 0.43, p < .001), species density (slope = 0.80, R2 = 0.33, p = .001) and the rarefied species richness per unit area (slope = 0.321, R2 = 0.32, p = .001). We added this supporting evidence on Lines 317-321:

“We thus suppose that habitat heterogeneity could also mitigate the loss of these relatively cold-adapted species as expected. Habitat diversity, including the observed number of species, the rarefied species richness per island, species density and the rarefied species richness per unit area, all increased significantly with island area instead of isolation in our system (Liu et al., 2020)”

Despite the general clear patterns found in the paper, there were some idiosyncratic responses. Those could be due to a multitude of factors which could be discussed a bit better to inform future research using a similar study design.

Thank you for these suggestions. We added a summary statement about the reasons for idiosyncratic responses on Lines 334-338:

“Overall, these idiosyncratic responses reveal several possible mechanisms in regulating species' climate responses, including resource demands and biological interactions like competition and predation. Future studies are needed to take these factors into account to understand the complex mechanisms by which habitat loss meditates species range shifts.”

Reviewer #1 (Recommendations For The Authors):

(1) Figure 1: I disagree that there should be a temporal trend in colonisation/extinction dynamics.

Thank you again for these thoughtful comments. We have explained in detail in the response to the Public Review.

(2) L 485-487: As explained before I disagree. I don't see why there needs to be a temporal trend in colonization and extinction.

Thank you again for these thoughtful comments. Because we can’t guarantee that the study system has reached equilibrium, changing rates of colonization-extinction over time is actually a much stronger test of thermophilization. More detailed statement can be seen in the response to the Public Review.

(3) L 141: which species' ecological traits?

Sorry for the confusion. The traits included continuous variables (dispersal ability, body size, body mass and clutch size) and categorical variables (diet, active layer, residence type). Specifically, we tested the correlation between STI and dispersal ability, body size, body mass and clutch size using Pearson correlation test. We also tested the difference in STI between different trait groups using the Wilcoxon signed-rank test for three Category variables: diet (carnivorous/ omnivorous/ herbivory), active layer (canopy/mid/low), and residence type (resident species/summer visitor). There is no significant difference between any two groups for each of the three category variables (p > 0.2). We added these on Lines 141-145:

“No significant correlation was found between STI and species’ ecological traits; specifically, the continuous variables of dispersal ability, body size, body mass and clutch size (Pearson correlations for each, |r| < 0.22), and the categorial variables of diet (carnivorous/omnivorous/herbivory), active layer (canopy/mid/low), and residence type (resident species/summer visitor)”

(4) L 143: CTIoccur and CTIabun were not defined before.

Because CTIoccur and CTIabun were first defined in Methods part (section 4.4), we change the sentence to a more general statement here on Lines 147-150:

“At the landscape scale, considering species detected across the study area, occurrence-based CTI (CTIoccur; see section 4.4) showed no trend (posterior mean temporal trend = 0.414; 95% CrI: -12.751, 13.554) but abundance-based CTI (CTIabun; see section 4.4) showed a significant increasing trend.”

(5) Figure 4: what is the dashed vertical line? I assume the mean STI across species?

Sorry for the unclear description. The vertical dashed line indicates the median value of STI for 60 species, as a separation of warm-adapted species and cold-adapted species. We have added these details on Lines 807-809:

“The dotted vertical line indicates the median of STI values. Cold-adapted species are plotted in blue and warm-adapted species are plotted in orange.”

(6) Figure 6: in the legend, replace 'points in blue' with 'points in blue/orange' or 'solid dots' or something similar.

Thank you for this suggestion. We changed it to “points in blue/orange” on Lines 823.

(7) L 176-176: unclear why the interaction parameters are particularly important for explaining the thermophilization mechanism: if e.g. colonization rate of warm-adapted species is constantly higher in less isolated islands, (and always higher than the extinction rate of the same species), it means that thermophilization is increased in less isolated islands, right?

Thank you for this question. This is also related to the question about “Why use temporal trends in colonization/extinction rate to test for thermophilization mechanisms”. Colonization-extinction over time is actually a much stronger test of thermophilization (more details refer to response to Public Review and Recommendations 1&2).

Based on this, the two main driving processes of thermophilization mechanism include the increasing colonization rate of warm-adapted species and the increasing extinction rate of cold-adapted species with year. The interaction effect between island area (or isolation) and year on colonization rate (or extinction rate) can tell us how habitat fragmentation mediates the year effect. For example, if the interaction term between year and isolation is negative for a warm-adapted species that increased in colonization rate with year, it indicates that the colonization rate increased faster on less isolated islands. This is a signal of a faster thermophilization rate on less-isolated islands.

(8) L201-203: this is only little supported by the results that actually show that there is NO significant interaction for most species.

Thank you for this comment. Although most species showed non-significant interaction effect, the overall trend is relatively consistent, this is especially true for the effect of isolation. To emphasize the “trend” instead of “significant effect”, we slightly modified this sentence in more rigorous wording on Lines 205-208: 

“We further found that habitat fragmentation influences two processes of thermophilization: colonization rates of most warm-adapted species tended to increase faster on smaller and less isolated islands, while the loss rates of most cold-adapted species tended to be exacerbated on less isolated islands.”

(9) Section 2.3: can't you have a population-level estimate? I struggled a bit to understand all the parameters of the MSOM (because of my lack of statistical/mathematical proficiency) so I cannot provide more advice here.

Thank you for raising this advice. We think what you are mentioning is the overall estimate across all species for each variable. From MSOM, we can get a standardized estimate of every variable (year, area, isolation, interaction) for each species, separately. Because the divergent or consistent responses among species are what we are interested in, we didn’t calculate further to get a population-level estimate.

(10) L 291: a dot is missing.

Done. Thank you for your correction.

(11) L 305, 315: a space is missing

Done

(12) L 332: how were these islands selected?

Thank you for this question. The 36 islands were selected according to a gradient of island area and isolation, spreading across the whole lake region. The selected islands guaranteed there is no significant correlation between island area and isolation (the Pearson correlation coefficient r = -0.21, p = 0.21). The biggest 7 islands among the 36 islands are also the only several islands larger than 30 ha in the whole lake region. We have modified this in the Method part on Lines 360-363.

“We selected 36 islands according to a gradient of island area and isolation with a guarantee of no significant correlation between island area and isolation (Pearson r = -0.21, p = 0.21). For each island, we calculated island area and isolation (measured in the nearest Euclidean distance to the mainland) to represent the degree of habitat fragmentation.”

(13) L 334: "Distance to the mainland" was used as a metric of isolation, but elsewhere in the text you argue that the observed thermophilization is due to interisland movements. It sounds contradictory. Why not include the average or shortest distance to the other islands?

Thank you very much for raising this comment. Yes, “Distance to the mainland” was the only metric we used for isolation. We carefully checked through the manuscript where the “interisland movement” comes from and induces the misunderstanding. It must come from Discussion 3.1 (n Lines 217-221): “Notably, when tested on the landscape scale (versus on individual island communities), only the abundance-based thermophilization trend was significant, indicating thermophilization of bird communities was mostly due to inter-island occurrence dynamics, rather than exogenous community turnover.”

Sorry, the word “inter-island” is not exactly what we want to express here, we wanted to express that “the thermophilization was mostly due to occurrence dynamics within the region, rather than exogenous community turnover outside the region”. We have changed the sentence in Discussion part on Lines 217-221:

“Notably, when tested on the landscape scale (versus on individual island communities), only the abundance-based thermophilization trend was significant, indicating thermophilization of bird communities was mostly due to occurrence dynamics within the region, rather than exogenous community turnover outside the region.”

Besides, I would like to explain why we use distance to the mainland. We chose the distance to the mainland as a measure of isolation based on the results of a previous study. One study in our system provided evidence that the colonization rate and extinction rate of breeding bird species were best fitted using distance to the nearest mainland over other distance-based measures (distance to the nearest landmass, distance to the nearest bigger landmass)(Si et al., 2014). Besides, their results produced almost identical patterns of the relationship between isolation and colonization/extinction rate(Si et al., 2014). That’s why we only selected “Distance to the mainland” in our current analysis and we do find some consistent patterns as expected. The plants on all islands were cleared out about 60 years ago due to dam construction, with all bird species coming from the mainland as the original species pool through a process called “relaxation”. This may be the reason why distance to the nearest mainland is the best predictor.

In Discussion part, we added the following discussion and talked about the other measures on Lines 292-299:

“As a caveat, we only consider the distance to the nearest mainland as a measure of fragmentation, consistent with previous work in this system (Si et al., 2014), but we acknowledge that other distance-based metrics of isolation that incorporate inter-island connections could reveal additional insights on fragmentation effects. The spatial arrangement of islands, like the arrangement of habitat, can influence niche tracking of species (Fourcade et al., 2021). Future studies should take these metrics into account to thoroughly understand the influence of isolation and spatial arrangement of patches in mediating the effect of climate warming on species.”

(14) L 347: you write 'relative' abundance but this measure is not relative to anything. Better write something like "we based our abundance estimate on the maximum number of individuals recorded across the nine annual surveys".

Thank you for this suggestion, we have changed the sentence on Lines 377-379:

“We based our abundance estimate on the maximum number of individuals recorded across the nine annual surveys.”

(15) L 378: shouldn't the formula for CTIoccur be (equation in latex format):

CTI{occur, j, t} =\frac{\sum_{i=1}^{N_{j,t}}STI_{i}}{N_{j,t}}

Where Nj,t is the total number of species surveyed in the community j in year t

Thank you very much for this careful check, we have revised it on Lines 415, 417:

“where Nj,t is the total number of species surveyed in the community j in year t.”

Reviewer #2 (Recommendations For The Authors):

(1) Line 76: "weakly"

Done. Thank you for your correction.

(2) Line 98: I suggest a change to this sentence: "For example, habitat fragmentation renders habitats to be too isolated to be colonized, causing sedentary butterflies to lag more behind climate warming in Britain than mobile ones"

Thank you for this modification, we have changed it on Lines 99-101.

(3) Line 101: remove either "higher" or "increasing"

Done, we have removed “higher”. Thank you for this advice.

(4) Line 102: "benefiting from near source of"

Done.

(5) Line 104: "emigrate"

Done.

(6) Introduction: I suggest making it more explicit what process you describe under the word "extinction". At first read, I thought you were only referring to the dieback of individuals, but you also included emigration as an extinction process. It also needs to be reworded in Fig 1 caption.

Thank you for this suggestion. Yes, we can’t distinguish in our system between local extinction and emigration. The observed “extinction” of cold-adapted species over 10 years may involve two processes that usually occur in order: first “emigration” and then if can’t emigrate or withstand, “real local dieback”. It should also be included in the legend of Figure 1, as you said. We have modified the legend in Lines 780-781:

“Note that extinction here may include both the emigration of species and then the local extinction of species.”

There is also one part in the Discussion that mentions this on Lines 287-291: “While we cannot truly distinguish in our system between local extinction and emigration, we suspect that given two islands equal except in isolation, and if both lose suitability due to climate change, individuals can easily emigrate from the island nearer to the mainland, while individuals on the more isolated island would be more likely to be trapped in place until the species went locally extinct due to a lack of rescue”.

(7) I also suggest differentiating habitat fragmentation (distances between islands) and habitat amount (area) as explained in Fahrig 2013 (Rethinking patch size and isolation effects: the habitat amount hypothesis) and her latter paper. This will help the reader what lies behind the general trend of fragmentation: fragmentation per se and habitat amount reduction.

Thank you for this suggestion! Habitat fragmentation in this study involves both habitat loss and fragmentation per se. We now give a general definition of habitat fragmentation on Lines 61-63:

“Habitat fragmentation, usually defined as the shifts of continuous habitat into spatially isolated and small patches (Fahrig, 2003), in particular, has been hypothesized to have interactive effects with climate change on community dynamics.”

(8) Line 136: is the "+-" refers to the standard deviation or confidence interval, I suggest being explicit about it once at the start of the results.

Thank you for reminding this. The "+-" refers to the standard deviation (SD). The modified sentence is now on Lines 135-139:

“The number of species detected in surveys on each island across the study period averaged 13.37 ± 6.26 (mean ± SD) species, ranging from 2 to 40 species, with an observed gamma diversity of 60 species. The STI of all 60 birds averaged 19.94 ± 3.58 ℃ (mean ± SD) and ranged from 9.30 ℃ (Cuculus canorus) to 27.20 ℃ (Prinia inornate), with a median of STI is 20.63 ℃ (Appendix 1—figure 2; Appendix 1—figure 3).”

(9) Line 143: please specify the unit of thermophilization.

The unit of thermophilization rate is the change in degree per unit year. Because in all analyses, predictor variables were z-transformed to make their effect comparable. We have added on Line 151:

“When measuring CTI trends for individual islands (expressed as °/ unit year)”

(10) Line 289: check if no word is missing from the sentence.

The sentence is: “In our study, a large proportion (11 out of 15) of warm-adapted species increasing in colonization rate and half (12 out of 23) of cold-adapted species increasing in extinction rate were changing more rapidly on smaller islands.”

Given that we have defined the species that were included in testing the third prediction in both Methods part and Result part: 15 warm-adapted species that increased in colonization rate and 23 cold-adapted species that increased in extinction rate. We now remove this redundant information and rewrote the sentence as below on Lines 300-302:

“In our study, the colonization rate of a large proportion of warm-adapted species (11 out of 15) and the extinction rate of half of old-adapted species (12 out of 23) were increasing more rapidly on smaller islands.”

(11) Line 319: I really miss a concluding statement of your discussion, your results are truly interesting and deserve to be summarized in two or three sentences, and maybe a perspective about how it can inform conservation practices in fragmented settings.

Thank you for this profound suggestion both in Public Review and here. We have added a paragraph to the end of the Discussion, stating how our results can inform conservation, on Lines 339-347:

“Overall, our findings have important implications for conservation practices. Firstly, we confirmed the role of isolation in limiting range shifting. Better connected landscapes should be developed to remove dispersal constraints and facilitate species’ relocation to the best suitable microclimate. Second, small patches can foster the establishment of newly adapted warm-adapted species while large patches can act as refugia for cold-adapted species. Therefore, preserving patches of diverse sizes can act as stepping stones or shelters in a warming climate depending on the thermal affinity of species. These insights are important supplement to the previous emphasis on the role of habitat diversity in fostering (Richard et al., 2021) or reducing (Gaüzère et al., 2017) community-level climate debt.”

(12) Line 335: I suggest " ... the islands has been protected by forbidding logging, ..."

Thanks for this wonderful suggestion. Done. The new sentence is now on Lines 365-366:

“Since lake formation, the islands have been protected by forbidding logging, allowing natural succession pathways to occur.”

(13) Line 345: this speed is unusually high for walking, check the speed.

Sorry for the carelessness, it should be 2.0 km/h. It has been corrected on Lines 375-376:

“In each survey, observers walked along each transect at a constant speed (2.0 km/h) and recorded all the birds seen or heard on the survey islands.”

(14) Line 351: you could add a sentence explaining why that choice of species exclusion was made. Was made from the start of the monitoring program or did you exclude species afterward?

We excluded them afterward. We excluded non-breeding species, nocturnal and crepuscular species, high-flying species passing over the islands (e.g., raptors, swallows) and strongly water-associated birds (e.g., cormorants). These records were recorded during monitoring, including some of them being on the shore of the island or high-flying above the island, and some nocturnal species were just spotted by accident.

We described more details about how to exclude species on Lines 379-387:

“We excluded non-breeding species, nocturnal and crepuscular species, high-flying species passing over the islands (e.g., raptors, swallows) and strongly water-associated birds (e.g., cormorants) from our record. First, our surveys were conducted during the day, so some nocturnal and crepuscular species, such as the owls and nightjars were excluded for inadequate survey design. Second, wagtail, kingfisher, and water birds such as ducks and herons were excluded because we were only interested in forest birds. Third, birds like swallows, and eagles who were usually flying or soaring in the air rather than staying on islands, were also excluded as it was difficult to determine their definite belonging islands. Following these operations, 60 species were finally retained.”

(15) Line 370: I suggest adding the range and median of STI.

Thanks for this good suggestion. The range, mean±SD of STI were already in the Results part, we added the median of STI there as well. The new sentence is now in Results part on Lines 137-139:

“The STI of all 60 birds averaged 19.94 ± 3.58 ℃ (mean ± SD) and ranged from 9.30 ℃ (Cuculus canorus) to 27.20 ℃ (Prinia inornate), with a median of 20.63 ℃ (Appendix 1—figure 2; Appendix 1—figure 3).”

(16) Figure 4.b: Is it possible to be more explicit about what that trend is? the coefficient of the regression Logit(ext/col) ~ year + ...... ?

Thank you for this advice. Your understanding is right: we can interpret it as the coefficient of the ‘year’ effect in the model. More specifically, the ‘year’ effect or temporal trend here is the ‘posterior mean’ of the posterior distribution of ‘year’ in the MSOM (Multi-species Occupancy Model), in the context of the Bayesian framework. We modified this sentence on Lines 811-813:

“ Each point in (b) represents the posterior mean estimate of year in colonization, extinction or occupancy rate for each species.”

(17) Figure 6: is it possible to provide an easily understandable meaning of the prior presented in the Y axis? E.g. "2 corresponds to a 90% probability for a species to go extinct at T+1", if not, please specify that it is the logit of a probability.

Thank you for this question both in Public Review and here. The value on the Y axis indicates the posterior mean of each variable (year, area, isolation and their interaction effects) extracted from the MSOM model, where the logit(extinction rate) or logit(colonization rate) was the response variable. All variables were standardized before analysis to make them comparable. So, positive values indicate positive influence while negative values indicate negative influence. Because the goal of Figure 6 is to display the negative/positive effect, we didn’t back-transform them. Following your advice, we thus modified the caption of Figure 6 (now renumbered as Figure 5, following a comment from Reviewer #3, to move Figure 5 to Figure 4c). The modified title and legends of Figure 5 are on Lines 817-820:

“Figure 5. Posterior estimates of logit-scale parameters related to cold-adapted species’ extinction rates and warm-adapted species’ colonization rates. Points are species-specific posterior means on the logit-scale, where parameters >0 indicate positive effects (on extinction [a] or colonization [b]) and parameters <0 indicate negative effects.”

(18) Line 773: points in blue only are significant? I suggest "points in color".

Thank you for your reminder. Points in blue and orange are all significant. We have revised the sentence on Line 823:

“Points in blue/orange indicate significant effects.”

These are all small suggestions that may help you improve the readability of the final manuscript. I warmly thank you for the opportunity to review this impressive study.

We appreciate your careful review and profound suggestions. We believe these modifications will improve the final manuscript.

Reviewer #3 (Recommendations For The Authors):

I have a few minor suggestions for paper revision for your otherwise excellent manuscript. I wish to emphasize that it was a pleasure to read the manuscript and that I especially enjoyed a very nice flow throughout the ms from a nicely rounded introduction that led well into the research questions and hypotheses all the way to a good and solid discussion.

Thank you very much for your review and recognition. We have carefully checked all recommendations and addressed them in the manuscript.

(1) L 63: space before the bracket missing and I suggest moving the reference to the end of the sentence (directly after habitat fragmentation does not seem to make sense).

Thank you very much for this suggestion. The missed space was added, and the reference has been moved to the end of the sentence. We also add a general definition of habitat fragmentation. The new sentence is on Lines 61-64:

“Habitat fragmentation, usually defined as the shifts of continuous habitat into spatially isolated and small patches (Fahrig, 2003), in particular, has been hypothesized to have interactive effects with climate change on community dynamics.”

(2) L 102: I suggest to write "benefitting ..." instead.

Done.

(3) L 103: higher extinction rates (add "s").

Done.

(4) L 104: this should probably say "emigrate" and "climate warming".

Done.

(5) L 130-133: this is true for emigration (more isolated islands show slower emigration). But what about increased local extinction, especially for small and isolated islands? Especially since you mentioned later in the manuscript that often emigration and extinction are difficult to identify or differentiate. Might be worth a thought here or somewhere in the discussion?

Thank you for this good question. I would like to answer it in two aspects:

Yes, we can’t distinguish between true local extinction and emigration. The observed local “extinction” of cold-adapted species over 10 years may involve two processes that usually occur in order: first “emigration” and then, if can’t emigrate or withstand, “real local dieback”. Over 10 years, the cold-adapted species would have to tolerate before real extinction on remote islands because of disperse limitation, while on less isolated islands it would be easy to emigrate and find a more suitable habitat for the same species. Consequently, it’s harder for us to observe “extinction” of species on more isolated islands, while it’s easier to observe “fake extinct” of species on less isolated islands due to emigration. As a result, the observed extinction rate is expected to increase more sharply for species on less remote islands, while the observed extinction rate is expected to increase relatively moderately for the same species on remote islands.

We have modified the legend of Figure 1 on Lines 780-781:

“Note that extinction here may include both the emigration of species and then the local extinction of species.”

There is also one part in the Discussion that mentions this on Lines 287-291: “While we cannot truly distinguish in our system between local extinction and emigration, we suspect that given two islands equal except in isolation, if both lose suitability due to climate change, individuals can easily emigrate from the island nearer to the mainland, while individuals on the more isolated island would be more likely to be trapped in place until the species went locally extinct due to a lack of rescue”.

Besides, you said “But what about increased local extinction, especially for small and isolated islands?”, I think you are mentioning the “high extinction rate per se on remote islands”. We want to test the “trend” of extinction rate on a temporal scale, rather than the extinction rate per se on a spatial scale. Even though species have a high extinction rate on remote islands, it can also show a slower changing rate in time.

I hope these answers solve the problem.

(6) L 245: I think this is the first time the acronym appears in the ms (as the methods come after the discussion), so please write the full name here too.

Thank you for pointing out this. I realized “Thousand Island Lake” appears for the first time in the last paragraph of the Introduction part. So we add “TIL” there on Lines 108-109:

“Here, we use 10 years of bird community data in a subtropical land-bridge island system (Thousand Island Lake, TIL, China, Figure 2) during a period of consistent climatic warming.”

(7) L 319: this section could end with a summary statement on idiosyncratic responses (i.e. some variation in the responses you found among the species) and the potential reasons for this, such as e.g. the role of other species traits or interactions, as well as other ways to measure habitat fragmentation (see main comments in public review).

Thank you for this suggestion both in Public Review and here. We added a summary statement about the reasons for idiosyncratic responses on Lines 334-338:

“Overall, these idiosyncratic responses reveal several possible mechanisms in regulating species' climate responses, including resource demands and biological interactions like competition and predation. Future studies are needed to take these factors into account to understand the complex mechanisms by which habitat loss meditates species range shifts.”

We only strengthen “habitat loss” here, because idiosyncratic responses mainly come from the mediating effect of habitat loss. For the mediating effect of isolation, the response is relatively consistent (see Page 8, Lines 183-188): “In particular, the effect of isolation on temporal dynamics of thermophilization was relatively consistent across cold- and warm-adapted species (Figure 5a, b); specifically, on islands nearer to the mainland, warm-adapted species (15 out of 15 investigated species) increased their colonization probability at a higher rate over time, while most cold-adapted species (21 out of 23 species) increased their extinction probability at a higher rate”.

(8) L 333: what about the distance to other islands? it's more of a network than a island-mainland directional system (Figure 2). You could address this aspect in the discussion.

Thank you for this good question again. Isolation can be measured in different ways in the study region. We chose distance to the mainland because it was the best predictor of colonization and extinction rate of breeding birds in the study region, and produced similar results like the other distance-based measures, including distance to the nearest landmass, distance to the nearest larger landmass (Si et al., 2014). We still agree with you that it’s necessary to consider more aspects of “isolation” at least in discussion for future research. In Discussion part, we addressed these on Lines 292-299. For more details refer to the response to Public Review.

(9) Figure 2: Is B1 one of the sampled islands? It is clearly much larger than most other islands and I think it could thus serve as an important population source for many of the adjacent smaller islands? Thus, the nearest neighbor distance to B1 could be as important in addition to the distance to the mainland?

Yes, B1 is one of the sampled islands and is also the biggest island. In previous research in our study system, we tried distance to the nearest landmass, to the nearest larger landmass and the nearest mainland, they produced similar results (For more details refer to the response to Public Review). We agree with you that the nearest neighbor distance to B1 could be a potentially important measure, but need further research. In our Discussion, we address these on Lines 292-299:

“As a caveat, we only consider the distance to the nearest mainland as a measure of fragmentation, consistent with previous work in this system (Si et al., 2014), but we acknowledge that other distance-based metrics of isolation that incorporate inter-island connections could reveal additional insights on fragmentation effects. The spatial arrangement of islands, like the arrangement of habitat, can influence niche tracking of species (Fourcade et al., 2021). Future studies should take these metrics into account to thoroughly understand the influence of isolation and spatial arrangement of patches in mediating the effect of climate warming on species.”

(10) L 345: 20km/h walking seems impressively fast? I assume this is a typo.

Sorry for the carelessness, it should be 2.0 km/h. it has been corrected on Lines 375-376:

“In each survey, observers walked along each transect at a constant speed (2.0 km/h) and recorded all the birds seen or heard on the survey islands.”

(11) L 485: I had difficulties fully understanding the models that were fitted here and could not find them in the codes you provided (which were otherwise very well documented!). Could you explain this modeling step in a bit more detail?

Thank you for your recognition! According to Line 485 in the online PDF version (Methods part 4.6.3), it says: “An increasing colonization trend of warm-adapted species and increasing extinction trend of cold-adapted species are two main expected processes that cause thermophilization (Fourcade et al., 2021). To test our third prediction about the mediating effect of habitat fragmentation, we selected warm-adapted species that had an increasing trend in colonization rate (positive year effect in colonization rate) and cold-adapted species that had an increasing extinction rate (positive year effect in extinction rate)…..”

We carefully checked the code in Figshare link and found that the MOSM JAGS code was not uploaded before. Very sorry for that. Now it can be found in the document [MOSM.R] at https://figshare.com/s/7a16974114262d280ef7. Hope the code, together with the modeling process in section 4.5 in the Methods can help to understand the whole modeling process. Besides, we would like to explain how to decide the temporal trend in colonization or extinction of each species related to Line 485. Let’s take the model of species-specific extinction rate for example:

In this model, “Island” was a random effect, “Year” is added as a random slope, thus allowing “year effect” (that is: the temporal trend) of extinction rate of species to vary with “island”. Further, the interaction effect between island variables (isolation, area) was added to test if the “year effect” was related to island area or isolation.

Because we are only interested in warm-adapted species that have a positive temporal trend in colonization and cold-adapted species that have a positive temporal trend in extinction, which are two main processes underlying thermophilizaiton, we choose warm-adapted species that have a positive year-effect in colonization, and cold-adapted species that has a positive year-effect in extinction. Hope this explanation and the JAGS code can help if you are confused about this part.

Hope these explanations can make it clearer.

(12) Figure 1: to me, it would be more intuitive to put the landscape configuration in the titles of the panels b, c, and d instead of "only" the mechanisms. E.g. they could be: a) fragmented islands with low climate buffering; b) small islands with low habitat heterogeneity; c) isolated islands with dispersal limitations?

It is also slightly confusing that the bird communities are above "island" in the middle of the three fragmented habitats - which all look a bit different in terms of tree species and structure which makes the reader first think that it has something to do with the "new" species community. so maybe worth rethinking how to illustrate the three fragmented islands?

We would like to thank you for your nice proposition. Firstly, it’s a good idea to put the landscape configuration in the title of the panels b, c, d. The new title (a) is “Fragmented islands with low climate buffering”, title (b) is “Small islands with low habitat heterogeneity”, and title (c) is “Isolated patches with dispersal limitations”.

Second, we realized that putting the “bird community” above “island” in the middle of the three patches is a bit confusing. Actually, we wanted to show bird communities only on that one island in the middle. The other two patches are only there to represent a fragmented background. To avoid misunderstanding, we added a sentence in the legend of Figure 1 on Lines 778-780:

“The three distinct patches signify a fragmented background and the community in the middle of the three patches was selected to exhibit colonization-extinction dynamics in fragmented habitats.”

(13) Figure 4: please add the description of the color code for panel a.

Sorry for the unclear description. The vertical dashed line indicates the median value of STI for 60 species, as a separation of warm-adapted species and cold-adapted species. We have added these details on Lines 807-809:

“The dotted vertical line indicates the median of STI values. Cold-adapted species are plotted in blue and warm-adapted species are plotted in orange.”

(14) Figure 5: You could consider adding this as panel c to Figure 4 as it depicts the same thing as in 4a but for CTI-abundance.

Thank you for this advice. We have moved the original Figure 5 to Figure 4c. Previous Figure 6 thus turned into Figure 5. All corresponding citations in the main text were checked to adapt to the new index. The new figure is now on Lines 801-815:

References

Ferraz, G., Russell, G. J., Stouffer, P. C., Bierregaard Jr, R. O., Pimm, S. L., & Lovejoy, T. E. (2003). Rates of species loss from Amazonian forest fragments. Proceedings of the National Academy of Sciences, 100(24), 14069-14073. doi:10.1073/pnas.2336195100

Fourcade, Y., WallisDeVries, M. F., Kuussaari, M., van Swaay, C. A., Heliölä, J., & Öckinger, E. (2021). Habitat amount and distribution modify community dynamics under climate change. Ecology Letters, 24(5), 950-957. doi:10.1111/ele.13691

Gaüzère, P., Princé, K., & Devictor, V. (2017). Where do they go? The effects of topography and habitat diversity on reducing climatic debt in birds. Global Change Biology, 23(6), 2218-2229. doi:10.1111/gcb.13500

Gonzalez, A. (2000). Community relaxation in fragmented landscapes: the relation between species richness, area and age. Ecology Letters, 3(5), 441-448. doi:10.1046/j.1461-0248.2000.00171.x

Haddad, N. M., Brudvig, L. A., Clobert, J., Davies, K. F., Gonzalez, A., Holt, R. D., . . . Collins, C. D. (2015). Habitat fragmentation and its lasting impact on Earth’s ecosystems. Science advances, 1(2), e1500052. doi:10.1126/sciadv.1500052

Richard, B., Dupouey, J. l., Corcket, E., Alard, D., Archaux, F., Aubert, M., . . . Macé, S. (2021). The climatic debt is growing in the understorey of temperate forests: Stand characteristics matter. Global Ecology and Biogeography, 30(7), 1474-1487. doi:10.1111/geb.13312

Si, X., Pimm, S. L., Russell, G. J., & Ding, P. (2014). Turnover of breeding bird communities on islands in an inundated lake. Journal of Biogeography, 41(12), 2283-2292. doi:10.1111/jbi.12379

Author response:

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

Reviewer #1 (Recommendations For The Authors): 

Figures 1 and 2. How do the authors know that the lysine mutations are specific to constitutive activity and not because it is causing the channel to be now voltage sensitive? 

As shown in the revised Figs. 1b, S2a, and 3b, TMEM16F I521K/M522K, TMEM16F I521E, and TMEM16A I546K/I547K spontaneously expose PS, respectively. Neither membrane depolarization nor calcium stimulation was introduced under these conditions and the cells were grown in calcium-free media after transfection to limit calcium-dependent activation. Our new experiments further demonstrate that TMEM16F T526K (Fig. 1b) and TMEM16A E551K (Fig. 3b), which are further away from the activation gate, exhibit either strongly attenuated or lack spontaneous lipid scrambling activity. According to these results, the gain-of-function mutants (TMEM16F

I521K/M522K/I521E and TMEM16A I546K/I547K) are indeed constitutively active. This constitutive scramblase activity is not due to a gain of voltage sensitivity as ion channel activity is also minimal around the resting membrane potential of a HEK cell (Fig. 1d, e and Fig. 3d, e).

The authors see very large currents of 5 -10 nA in their electrophysiology experiments in Figures 2D and 3D. I understand that Figure 2D are whole-cell recordings but are the authors confident that the currents that they are recordings from the mutants are indeed specific to TMEM16A. More importantly, in Figure 3D they see 3-5nA currents in insideout patches, which is huge. They have no added divalent in their bath solution, which could lead to larger single-channel amplitudes, but 3-5nA seems excessive. Some control to demonstrate that these are indeed OSCA1.2 currents is important. 

TMEM16A and TMEM16F are well-known for their high cell surface expression. Therefore, the current amplitude is usually huge even in excised inside-out or outside-out patches—please see our previous publications for details: 1) 10.1016/j.cell.2012.07.036, 2) 10.7554/eLife.02772, 3) 10.1038/s41467-019-11784-8, 4) 10.1038/s41467-019-09778-7, 5) 10.1016/j.celrep.2020.108570, 6) 10.1085/jgp.202012704, and 7) 10.1085/jgp.202313460. 

HEK293 cells do not have endogenous TMEM16A (https://doi.org/10.1038/nature07313, 10.1016/j.cell.2008.09.003 , DOI: 10.1126/science.1163518). It therefore serves as a widely used cell line for studying TMEM16A biophysics. As overexpressing the WT control barely elicited any obvious current in 0 Ca2+ (Fig. 3d), there is no doubt that the large outward-rectifying current (hallmark of CaCC) in the revised Fig. 3d (previous Fig. 2D) was elicited from the mutant TMEM16A channels. The strong outward rectification also rules out the possibility of this being leak current.

Regarding Fig. 4d (previous Fig. 3D), OSCA1.2 has excellent surface expression as shown in Fig. 4b. OSCA1.2 also has much higher single channel conductance (121.8 ± 3.4 pS, 10.7554/eLife.41844) than TMEM16A (~3-8 pS) and TMEM16F (<1 pS). Therefore, recording nA OSCA1.2 current from excised patches is normal given larger OSCA1.2 current at depolarized voltages than the current recorded at hyperpolarized voltages (please see our explanation in the next response). As the reviewer pointed out, lack of divalent ions in our experimental conditions may also partially contribute to the large conductance. To further verify, we conducted mock transfection recordings (please see Author response image 1 below). WT- but not mock (GFP)transfected cells gave rise to large current, further supporting that the recorded current was indeed through OSCA1.2. 

Author response image 1.

Representative inside-out currents for mock (GFP)- and OSCA1.2 WT-transfected cells. OSCA1.2 is responsible for nA currents elicited by the pressure and voltage protocols shown.

Figure 3D and 5D. Most of the traces and current quantification is done at positive potentials and is outward current. Do the authors observe inward currents? It is difficult to judge by the figures since currents are so large. OSCA/TMEM63s are cationic channels and all published data on these channels have demonstrated robust inward currents at negative, physiologically relevant potentials. The lack of inward currents but only large outward currents suggests that these mutations could be doing something else to the channel. 

Yes. We indeed observe inward current at negative holding potentials under pressure clamp (Author response image 2). However, mechanosensitive OSCA and TMEM63A channels are also voltage dependent. Their outward current is an order of magnitude larger at depolarized voltages (e.g., Author response image 2, also 10.7554/eLife.41844, see Fig. 1H). 

Author response image 2.

Voltage-dependent rectification of OSCA1.2 current. a. Representative OSCA1.2 trace (bottom) elicited by a voltage-ramp under -50 mmHg (top). b. The difference in inward and outward current amplitudes. 

We found that quantifying the OSCA1.2 outward current has advantages over the inward current. Usually, using the gold standard pressure clamp protocol at negative holding voltages, peak inward current amplitude is quantified. However, OSCA inward current quickly inactivates (10.7554/eLife.41844, see Fig. 1C). This makes robust quantification and comparison with mutant channels difficult. Holding the membrane at a constant pressure and measuring OSCA1.2 G-V overcomes these issues associated with the classical inward current measurements. The large depolarization-driven outward current does not inactivate, and robust tail current (Response Fig. 1, 2) allows us to construct G-V relationships. We found quantifying mutants’ voltage dependence at constant pressure is more consistent than quantifying pressure dependence at constant voltage. These advantages make our new protocol preferable to the commonly used gold standard pressure clamp protocol for characterizing and comparing the gating mutations identified in this manuscript. 

Figure 3 and 5. Why are mechanically activated currents being recorded at random pressure stimuli (-50 mmHg for OSCA) and (-80 mmHg for Tmem63a)? The gold standard in the field is to run an entire pressure response curve. Given that only outward currents are observed at membrane potentials +120mV and above at 0mmHg, this questions whether they are indeed constitutively active. 

As we explained in the previous response, both voltage and membrane stretch activate OSCA/TMEM63A channels. We found measuring voltage dependence under constant pressure provided more consistent quantification than the gold standard pressure response protocol. This may be due to the variability of applied membrane tension under repeated stretches versus the more consistent applied voltage. Additionally, we chose -50 mmHg and -80 mmHg to reflect the reported differences in half-maximal pressures between OSCA1.2 and TMEM63A (e.g., P50 ~55 mmHg for 1.2 and ~61 mmHg for 63A in 10.7554/eLife.41844 versus ~86 mmHg for 1.2 and -123 mmHg for 63A in 10.1016/j.neuron.2023.07.006).

We also used higher pressure in cell attached mode to increase TMEM63A current amplitudes, which are usually tiny.  We have updated our method section (Lines 329334) to further clarify why we used these protocols. 

Please note that in TMEM16 proteins, ions and lipids might not always co-transport.

This means that under certain conditions, only one type of substrate may go through. For instance, in WT TMEM16F, Ca2+ stimulation can easily trigger PS exposure at resting membrane potential. No ionic currents are elicited until strong depolarization is applied. Similarly, the TMEM16F GOF mutations spontaneously transport lipids, leading to loss of lipid asymmetry (Fig. 1b, c). However, in 0 Ca2+, these TMEM16F mutant channels still need strong depolarization for ion conduction (Fig. 1d, e). Although the detailed mechanism still needs to be further investigated, the OSCA1.2 and TMEM63A GOF mutations share similar features with TMEM16 proteins, exhibiting ion conduction under high pressures and depolarizing voltages, yet constitutively active scrambling.  

Some clarity is needed for their choice of residues. I understand that a lot of this is also informed by the structures of these ion channels. According to the alignment shown in Supplementary Figure 1, they chose LA for OSCA1.2, which is in line with the IM (TMEM16F) and II(TMEM16A) residues but for Tmem63a they chose the hydrophobic gate residue W and S. Was the A476 tested? Also, OSCA1.2 already has a K in the hydrophobic gating residue region. How do the authors reconcile this with their model? 

We appreciate this critical comment. We have included the characterization of TMEM63A A476K (Fig. 6, corresponding to M522 in 16F, I547 in 16A, and A439 in OSCA1.2). Interestingly, A476K transfected cells did not show obvious spontaneous PS exposure yet exhibited a modest shift in V50 comparable to W472K and S475K. These differences may reflect the high-tension activated nature of the TMEM63 proteins (10.1016/j.neuron.2023.07.006) as compared to OSCA1.2, where the corresponding mutation (A439K, Fig. 4b, c) showed very little spontaneous activity and required hypotonic stimulation to promote more robust PS exposure (Fig. 5). 

Furthermore, as we showed in Figs. 1b-c and 3b-c, there is a lower limit (towards the Cterminus) of the TM 4 lysine mutation effect, which becomes insufficient to cause a constitutively open pore for spontaneous lipid scrambling. It is possible that TMEM63A A476K represents the lower limit of TM 4 mutations that can convert TMEM63A into a spontaneous lipid scramblase.  

Regarding OSCA1.2 K435 and TMEM63A W472, these sites correspond to the hydrophobic gate residues on TM 4 in TMEM16F (F518, Fig. 1a) and TMEM16A (L543, Fig. 3a) so it is unsurprising to us that a lysine mutation at this site causes constitutive scramblase activity in TMEM63A (Fig. 6b, c). For OSCA1.2, it is more intriguing since this residue is already a lysine (K435). In Supplementary Fig. 5 our new experiments show that neutralizing K435 with leucine (K435L) in the background of L438K significantly attenuates spontaneous PS exposure from ~63% PS positive for L438K alone (two lysine residues) to ~31% for K435L/L438K (one lysine). One the other hand, the K435L mutation by itself is also insufficient to induce PS exposure. Therefore, the endogenous lysine at residue 435 has an additive effect on the spontaneous scramblase activity of L438K. We believe the explanation for this result lies in experiments conducted in model transmembrane helices, which have shown that stacking hydrophilic side chains within the membrane interior promotes trans-bilayer lipid flipping (see 10.1248/cpb.c22-00133). 

These same studies also support our observation (10.1038/s41467-019-09778-7) that highly hydrophilic side chains (such as lysine or glutamic acid) accelerate trans-bilayer lipid flipping more effectively than hydrophobic side chains such as isoleucine or alanine (Author response image 3, see also 10.1021/acs.jpcb.8b00298).

Author response image 3.

Trans-bilayer lipid flipping rates (kflip) accelerate with increasing side chain hydropathy for a residue placed in the center of a model transmembrane helical peptide

How do the authors know that osmotic shock is indeed activating OSCA1.2 and TMEM63A? If they can record from the channels then electrophysiology data that confirms activation of the channel in the presence of hypoosmotic shock will strengthen the osmolarity active scramblase activity demonstrated in Figure 4. So far, there is conclusive data showing that they are mechanically activated but conclusive electrophysiological data for OSCA/TMEM63 osmolarity activation is not described yet, including the reference (38) they indicate in line 132. Although osmotic shock can perturb mechanical properties of the membrane it can also activate volume-regulated anion channels, which are also present in HEK cells. 

Thank you for raising this important question. While reference 38, (now reference 39) shows direct electrophysiological evidence of hypertonicity-induced current (e.g., Fig. 4 f, g, i, and j in 10.1038/nature13593), direct electrophysiological evidence that OSCA/TMEM63 can be activated by hypotonic stimulation is still missing. To address this question, we conducted whole-cell patch clamp experiments on mocktransfected and OSCA1.2 WT-transfected cells stimulated with 120 mOsm/kg hypotonic solution, comparable to the same conditions as hypotonic-induced scrambling shown in Fig. 5. As shown in Supplementary Fig. 6, our whole-cell recording detected a slowly evolving yet robust outward rectifying current in OSCA1.2-transfected cells, which was not observed in mock transfected cells. 

To avoid the contamination from endogenous SWELL osmo-/volume-regulated chloride channels, our new experiment used 140 mM Na gluconate to replace NaCl in both the pipette and the bath solution. Because SWELL/VRAC channels are minimally permeable to gluconate anions (e.g., 10.1007/BF00374290), we conclude that hypotonic stimulation can indeed activate OSCA1.2 albeit with perhaps lower efficiency compared to mechanical stimulation.  

Minor comments 

What is the timeline for the scramblase assay for all the experiments (except Figure 4)? How long is the AnnexinV incubated before imaging? 

Thank you for pointing out this point where we have not provided sufficient detail. Cells were imaged in the scramblase assay (including in Fig. 4, now revised Fig. 5) in AnnexinV-containing buffer immediately and without a formal incubation period because AnnexinV binding to exposed PS proceeds rapidly. We have included additional detail in the methods section to eliminate any confusion (Lines 310-312).

In some places of the document, it says OSCA/TMEM63, and in other places, it is denoted as TMEM63/OSCA. The literature so far has always called the family OSCA/TMEM63- please stay consistent with the field. 

Thank you for pointing this out, we have corrected these instances to be consistent with the field.   

Reviewer #2 (Recommendations For The Authors): 

(1) The authors' statement that the channel/scramblase family members have a relatively low "energetic barrier for scramblase" activity needs further support. While mutating the hydrophobic channel gate certainly could destabilize ion conduction to cause a GOF effect on channel activity, it is still not clear why scramblase activity, which is tantamount to altered permeation, happens in the mutant channels. Are permeation and channel gating (opening) coupled in these channels? If so, what is the basis for the coupling? Is scramblase activity only observed when the gating is destabilized or are they separable? 

We appreciate these great questions. For the question about the ‘energetic barrier’ statement, please see our response to point (3) where we have carried out MD simulations of the OSCA1.2 WT and L438K mutant to provide insight into how the permeation pathway is altered by these mutations. 

Regarding why TMEM16A can be converted into a scramblase, we use the extensively studied TMEM16 proteins as examples to improve our current understanding of OSCA/TMEM63 proteins. For further details please see our original paper (10.1038/s41467-019-09778-7) and our review (10.3389/fphys.2021.787773), which are summarized as follows: 

(1) The “neck region”, consisting of the exofacial halves of TMs 3-6, form the poregate region for both ion and lipid permeation (Author response image 4B). In the closed state, the neck region is constricted and TMs 4 and 6 interact with each other, preventing substrate permeation. The hydrophobic inner activation gate that we identified (10.1038/s41467-019-09778-7) resides right underneath the inner mouth of the neck region, controlling both ion and lipid permeation scrambling. 

(2) Based on our functional observations and the available scramblase structures of TMEM16 proteins in multiple conformations, we proposed a clamshell-like gating model to describe TMEM16 lipid scrambling (Author response image 4D). According to this model, Ca2+-induced conformational changes weaken the TM 4/6 interface. This promotes the separation of the two transmembrane segments, analogous to the opening of a clam shell, allowing a membrane-spanning groove to facilitate permeation of the lipid headgroup.

(3) For the CaCC, TMEM16A, Ca2+ binding dilates the pore. However, the binding energy likely cannot open the TM 4/6 interface at the neck region so, in the absence of groove formation, only Cl- ions but not lipids can permeate. (Pore dilation model, Author response image  4C). 

(4) Introducing charged residues near the inner activation gate disrupts the neck region, potentially by weakening the hydrophobic interactions between TMs 4 and 6. This mutational effect results in constitutively active TMEM16F scramblases and enables spontaneous lipid permeation in the TMEM16A CaCC. 

(5) In our revision, we tested additional mutations with different side chain properties (Supplementary Fig. 2), validating previous findings by us (10.1038/s41467-01909778-7) and others (10.1038/s41467-022-34497-x) that gate disruption increases with the side chain hydropathy of the mutation. 

(6) We further extended lysine mutations to two helical turns below the inner activation gate on TM 4 and identified a lower limit for mutation-induced spontaneous scramblase activity in TMEM16F and TMEM16A (Figs. 1b, c and 3b, c, respectively). Together, all these points lend additional support to our proposed gating models for TMEM16 proteins, which we postulate may also relate to the OSCA/TMEM63 family based on the evidence provided in our manuscript.

Author response image 4.

Model of gating (and regulatory) mechanisms in the TMEM16 family. (B) overall architecture and proposed modules, (C) pore-dilation gating model for CaCCs, (D) Clamshell gating model for CaPLSases.

Regarding the relationship between ion and lipid permeation through TMEM16 scramblases, the following is the summary of our current understanding: 

(1) Functionally, ion and lipid permeation are not necessarily obligatory to each other. This is evidenced by our previous biophysical characterizations of TMEM16F ion channel and lipid scramblase activities. Ca2+ can trigger TMEM16F lipid scrambling at resting membrane potentials, however, Ca2+ alone is insufficient to record TMEM16F current. Strong membrane depolarization synergistically with elevated intracellular Ca2+ is required to activate ion permeation. Based on these observations, we postulate that ions and lipids may have different extracellular gates, despite sharing an inner activation gate (10.1038/s41467-019-09778-7). Ca2+ alone may sufficiently open the inner gate (and extracellular gate) for lipids, whereas depolarization is likely required to open the extracellular gate and allow ion flux. Further structure-function studies are needed to test this hypothesis. 

(2) Structurally, the open conformation of TMEM16 scramblases such as the fungal orthologs and human TMEM16K (Supplementary Fig. 1 b-d) are widely open, which allows lipid and ion co-transport. Ion and lipid co-transport has also been demonstrated in various MD simulations (e.g., 10.7554/eLife.28671, 10.3389/fmolb.2022.903972, and 10.1038/s41467-021-22724-w)

(3) Functionally, we (10.1085/jgp.202012704) and others (10.7554/eLife.06901.001) have measured dual recording of channel and scramblase activities, also demonstrating that ions and lipids are co-transported simultaneously when the proteins are fully activated.

(4) In this manuscript, we also provide multiple examples (TMEM16F in Fig. 1, TMEM16A in Fig. 3, OSCA1.2 in Fig. 4, and TMEM63A in Fig. 6) of mutations showing spontaneous phospholipid scramblase activities, yet their channel activities require strong depolarization or, in the case of TMEM63A, high pressures to be elicited.

Together, this new evidence further supports our hypothesis that there might be multiple gates for ion and lipid permeation, in addition to the shared inner gate we previously identified. We hope these detailed explanations help convey the intricacy of these intriguing questions. Of course, future studies are needed to test our hypothesis and elucidate the complex relationship between ion and lipid permeation of these proteins. 

(2) One weakness in the experimental approach is the very limited number of substitutions used to infer the conclusion regarding the energetic barrier and other conclusions relating to scramblase activity. Additional substitutions of charged and polar amino acids at the hydrophobic gate would be helpful in illuminating the molecular determinants of the GOF phenotype and also reveal varying patterns of lipid permeation which could be enormously informative. These additional mutations for analysis of TMEM16F and OSCA should be added to the study. 

We appreciate these great suggestions which were shared by multiple reviewers. We have included our duplicated response below.

“Response to reviewers 2 & 3: In our 2019 paper (10.1038/s41467-019-09778-7), we have systematically tested the side chain properties at the inner activation gate of TMEM16F on lipid scrambling activity (Response Fig. 6) and, since then, these results have been supplemented by others as well (10.1038/s41467-022-34497-x). In summary, mutating the inner activation gate residues to polar or charged residues generally results in constitutively activated scramblases without requiring Ca2+ (Fig 5a in 10.1038/s41467-019-09778-7). Because these residues form a hydrophobic gate, introducing smaller side chains via alanine substitution are also gain-of-function with the Y563A mutant as well as the F518A/Y563A/I612A variant being constitutively active (Fig. 3a in 10.1038/s41467-019-09778-7). Meanwhile, mutating these gate residues to hydrophobic amino acids causes no change for I612W, a slight gain-of-function for F518W, slight loss-of-function of F518L, and complete loss-of-function for Y563W (Fig. 4b in 10.1038/s41467-01909778-7). These findings clearly demonstrate that the side-chain properties are critical for regulating the gate opening. Charged mutations including lysine and glutamic acid are the most effective to promote gate opening (Fig 5a in 10.1038/s41467-019-09778-7).

Similarly, others have observed that side chain hydropathy at the F518 site in TMEM16F correlates with shifts in the Ca2+ EC50 (Fig. 2 of 10.1038/s41467-022-34497-x). Note that this publication resolved the structure of the TMEM16F F518H mutant, revealing a previously unseen conformation that we have highlighted in Supplementary Fig. 1e and discussed in lines 235-238. Please also see our response to Reviewer #1 above, where we discuss discoveries in model transmembrane helical peptide systems showing that transbilayer lipid flipping rates correlate with side chain hydropathy (Author response image 3), distance between stacked hydropathic residues (schematic in 10.1248/cpb.c22-00133), and even helical angle between stacked side chains (not show). 

Following the reviewers’ suggestions, we have tested additional mutations in alternative locations and with different side chains.  

(1) We have added data for TMEM16F I521A and I521E to demonstrate a similar effect of alternative side chains to what has previously been reported by us and others. We found that I521A failed to show spontaneous scrambling activity (Supplementary Fig. 2), yet I521E (Supplementary Fig. 2) is a constitutively active lipid scramblase, similar to I521K (Fig. 1). This further demonstrates that gate disruption correlates with the side chain hydropathy and that this site lines a critical gating interface.

(2) We also added lysine mutations two helical turns below the conserved inner activation gate for TMEM16F T526 (Fig. 1), TMEM16A E551 (Fig. 3). We found that there is indeed a lower limit for the observed effect in TMEM16, where lysine mutations no longer induce spontaneous lipid scrambling activity. This indicates that when TM 4/6 interaction is weaker toward intracellular side (Figs. 1a, 3a), the TM 4 lysine mutation loses the ability to promoting lipid scrambling by disrupting the TM 4/6 interface to enable clamshell-like opening of the permeation pathway. 

(3) We added a TMEM16F lysine mutation on TM 6 at residue I611 (Fig. 2). Similar to I612K (Response Fig. 6), I611K also leads to spontaneous lipid scrambling and enhanced channel activity in the absence of calcium (Fig. 2). This shows that charged mutations along TM 6 can also promote lipid scrambling, strengthening our model that hydrophobic interactions along the TM 4/6 interface are critical for gating and lipid permeation.”

(3) Related to the above point, it would be enormously useful to perform even limited computational modelling to support the "energetic barrier" statement. Specifically, can the authors model waters in the putative pore to examine water occupancy in the WT and mutant channels to better understand how the barrier for ions and lipids is altered in the TMEM16? 

We appreciate this suggestion and have now conducted atomistic MD simulations of OSCA1.2 WT and L438K mutant for ~1 μs (Supplementary Fig. 4). The simulations revealed, elevated water occupancy in the pore region of the L438K mutant, likely due to a widening at the TM 4/6 interface. Conversely, the WT interface remained constricted, largely disallowing water occupancy. These computational results support our previously proposed clamshell-like gating model for TMEM16 scramblases and provide strong support that the L438K mutation is disrupting the interaction of the TM 4/6 interface, in turn reducing the energetic barrier for both ion and lipid permeation. 

(4) I am puzzled about the ability of OSCA and the TMEM63 proteins which are cation channels to conduct negatively charged lipids. How can the pore be selective for cations and yet permeate negatively charged molecules when lipids are presented? 

This is a great question. TMEM16 scramblase (as well as other known scramblases, such as the Xkr and Opsin families) are surprisingly non-selective to phospholipids (all major phospholipid species, not just anionic lipids like PS). It is still debated whether lipid headgroups indeed insert into an open pore or hydrophilic groove (Response Fig. 5), or if they may traverse the bilayer by the so-called ‘out-of-groove’ model. Regardless of the model, the consensus is that Ca2+-induced conformational changes catalyze lipid permeation and the mutations we have introduced are designed to mimic these conformational changes by separating the TM 4/6 interface.

Additionally, TMEM16F channel activity was first characterized as cation non-selective (10.1016/j.cell.2012.07.036), similar to OSCA/TMEM63s, which may even exhibit some chloride permeability (10.7554/eLife.41844.001). Thus, it appears as though scramblase activity is agnostic to headgroup charge and compatible with both a mutant anion channel (TMEM16A) and mutant cation channels (TMEM16F, OSCA1.2, and TMEM63A), however, more detailed structural, functional, and computational studies are needed to further clarify ion and lipid co-transport mechanisms.  

(5) Do pore blockers like Gd3+ which block permeation also inhibit the scramblase activity of the mutant channels? This should be tested for the mutant channels. 

While extracellular Gd3+ has been previously reported as an inhibitor of OSCA1.2 (10.7554/eLife.41844.001), we did not observe this effect (Author response image 5), but instead saw inhibition by intracellular Gd3+ (Author response image 6). Given this discrepancy, we did not test Gd3+ inhibition of the OSCA1.2 scramblases, but instead tested Ani9, a paralog-specific inhibitor of TMEM16A, on the TMEM16A I546K gain-offunction and found it attenuated both ion channel and phospholipid scramblase activities (Supplementary Fig. 3).

Author response image 5.

200 µM Gd3+ext fails to inhibit OSCA1.2 currents in cell-attached patches. Pressure-elicited peak currents (n=6 each). Statistical test is an unpaired Student’s t-test.

Author response image 6.

200 µM Gd3+int completely inhibits OSCA1.2 currents in inside-out patches. (a) representative traces in before (black), during (red), and after (blue) Gd3+ application. (b) Representative application timecourse. (c) Quantification of peak currents (n=8 each). Statistical test is one-way ANOVA.

Minor: 

- Some of the current amplitudes shown in Figures 2 and 3 are enormous. Is liquid junction potential corrected in these experiments? If not, it would be preferable to correct this to avoid voltage errors. 

Thanks for the question. The large current amplitude is due to 1) great surface expression of the proteins; 2) large single channel conductance of OSCA channels, 3) much larger current at positive voltages for OSCA channels. Our control experiment showed that WT TMEM16A at 0 Ca2+ did not give rise to any current (Fig. 3d), further demonstrating that the large current was not due to liquid junction potential. For the OSCA recordings, we also did not observe current in mock-transfected cells, further excluding the possible interference of liquid junction potential (Response Fig. 1)

- Related, authors could consider adding some evidence using selective pharmacology to support the conclusions that the observed currents arise from TMEM or OSCA channels. 

Thanks for the suggestion. As mentioned above, we have added experiments with Ani9, a specific inhibitor of TMEM16A, in Supplementary Fig. 3. We found that Ani9 robustly attenuated both ion channel and phospholipid scramblase activities for the TMEM16A I546K gain-of-function mutant. This is also consistent with our previous publication (10.1038/s41467-019-09778-7), where Ani9 efficiently inhibited the TMEM16A L534K mutant scramblases. Additionally, we have provided mock controls (Response Fig. 1, Fig. 6d, e) to show that the observed currents are indeed attributable to OSCA1.2 and TMEM63A.

Reviewer #3 (Recommendations For The Authors): 

Given that the authors postulate that the introduction of a positive charge via the lysine side chain is essential to the constitutive activity of these proteins, additional mutation controls for side chain size (e.g. glutamine/methionine) or negative charge (e.g. glutamic acid), or a different positive charge (i.e. arginine) would have strengthened their argument. To more comprehensively understand the TM4/TM6 interface, mutations at locations one turn above and one turn below could be studied until there is no phenotype. In addition, the equivalent mutations on the TM6 side should be explored to rule out the effects of conformational changes that arise from mutating TM4 and to increase the strength of evidence for the importance of side-chain interactions at the TM6 interface. 

We appreciate these great suggestions which were shared by multiple reviewers. We have included our previous responses below.

“Response to reviewers 2 & 3: In our 2019 paper (10.1038/s41467-019-09778-7), we have systematically tested the side chain properties at the inner activation gate of TMEM16F on lipid scrambling activity (Response Fig. 6) and, since then, these results have been supplemented by others as well (10.1038/s41467-022-34497-x). In summary, mutating the inner activation gate residues to polar or charged residues generally results in constitutively activated scramblases without requiring Ca2+ (Fig 5a in 10.1038/s41467-019-09778-7). Because these residues form a hydrophobic gate, introducing smaller side chains via alanine substitution are also gain-of-function with the Y563A mutant as well as the F518A/Y563A/I612A variant being constitutively active (Fig. 3a in 10.1038/s41467-019-09778-7). Meanwhile, mutating these gate residues to hydrophobic amino acids causes no change for I612W, a slight gain-of-function for F518W, slight loss-of-function of F518L, and complete loss-of-function for Y563W (Fig. 4b in 10.1038/s41467-01909778-7). These findings clearly demonstrate that the side-chain properties are critical for regulating the gate opening. Charged mutations including lysine and glutamic acid are the most effective to promote gate opening (Fig 5a in 10.1038/s41467-019-09778-7).

Similarly, others have observed that side chain hydropathy at the F518 site in TMEM16F correlates with shifts in the Ca2+ EC50 (Fig. 2 of 10.1038/s41467-022-34497-x). Note that this publication resolved the structure of the TMEM16F F518H mutant, revealing a previously unseen conformation that we have highlighted in Supplementary Fig. 1e and discussed in lines 235-238. Please also see our response to Reviewer #1 above, where we discuss discoveries in model transmembrane helical peptide systems showing that transbilayer lipid flipping rates correlate with side chain hydropathy (Author response image 3), distance between stacked hydropathic residues (schematic in 10.1248/cpb.c22-00133), and even helical angle between stacked side chains (not show). 

Following the reviewers’ suggestions, we have tested additional mutations in alternative locations and with different side chains.  

(1) We have added data for TMEM16F I521A and I521E to demonstrate a similar effect of alternative side chains to what has previously been reported by us and others. We found that I521A failed to show spontaneous scrambling activity (Supplementary Fig. 2), yet I521E (Supplementary Fig. 2) is a constitutively active lipid scramblase, similar to I521K (Fig. 1). This further demonstrates that gate disruption correlates with the side chain hydropathy and that this site lines a critical gating interface.

(2) We also added lysine mutations two helical turns below the conserved inner activation gate for TMEM16F T526 (Fig. 1), TMEM16A E551 (Fig. 3). We found that there is indeed a lower limit for the observed effect in TMEM16, where lysine mutations no longer induce spontaneous lipid scrambling activity. This indicates that when TM 4/6 interaction is weaker toward intracellular side (Figs. 1a, 3a), the TM 4 lysine mutation loses the ability to promoting lipid scrambling by disrupting the TM 4/6 interface to enable clamshell-like opening of the permeation pathway. 

(3) We added a TMEM16F lysine mutation on TM 6 at residue I611 (Fig. 2). Similar to I612K (Response Fig. 6), I611K also leads to spontaneous lipid scrambling and enhanced channel activity in the absence of calcium (Fig. 2). This shows that charged mutations along TM 6 can also promote lipid scrambling, strengthening our model that hydrophobic interactions along the TM 4/6 interface are critical for gating and lipid permeation.”

The experiments for OSCA1.2 osmolarity effects on gating and scramblase in Figure 4 could be improved by adding different levels of osmolarity in addition to time in the hypotonic solution.

We thank the reviewer for this excellent suggestion. We extensively tested this idea and found evidence (Response Fig. 10) that intermediate osmolarity (220 and 180 mOso/kg) also can enhance the scramblase activity of the A439K mutant, albeit to a milder extent compared to 120 mOso/kg stimulation. This suggests that swellinginduced membrane stretch may proportionally induce A439K activation and lipid scrambling. Due to the relatively mild sensitivity of OSCA to osmolarity and the variations induced by the experimental conditions, we believe it is better to not include this data to avoid overclaiming. We hope the reviewer would agree. 

Author response image 7.

AnV intensities of WT- and A439K-transfected cells after 10 minutes of hypotonic stimulation at the listed osmolarities.

Some confocal images appear to be rotated relative to each other (e.g. Figures 2b and 3b).

Thank you for identifying these errors, they are corrected in the revision.

Author response:

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

Public Reviews:

We wish to thank the Reviewers for their critical analysis of the article and for their suggestions and comments.

In addition and beside the point-by-point answer to the Reviewers, we wish here to emphasize on three essential points that have been raised: First, we never intended (nor pretended) to address the incidence of the two EHT cell emergence processes on downstream fate, after release from the aortic floor (see for example the last paragraph of our initially submitted manuscript). We only wished to bring evidence on cell biological heterogeneity of the HE, particularly relying on cell polarity control and polarity reestablishment/reinforcement in the case of EHT pol+ cells, thus leading to emergence morphodynamic complexity. In the general context of cell extrusion in which all polarity features are generally downregulated, these are remarkable features.

Second, we inform the Reviewers that we have performed a major revision of the work on the Pard3 proteins issue the outcome of which, hopefully, substantiates significantly the idea of a tuning of cell polarity features in the HE and all along the EHT time-window, for supporting EHT pol- and EHT pol+ types of emergence. To achieve this, we entirely revised the experimental strategy to increase specificity and sensitivity of detection of Pard3 protein isoforms expressed in the vascular system, based on endothelial FACS-sorting, qRT-PCR and single-molecule whole mount in situ hybridization using RNAscope. Importantly, we wish to stress that, by addressing Pard3 proteins, we initially aimed at substantiating our observations on the localization of our podxl2 construct (del-podxl2) used to label apical membranes. Hence, we sought to bring correlative evidence on the variation of expression of polarity proteins at early and later time points of the EHT time-window (suggesting tightly regulated expression control of polarity determinants, possibly at the mRNA level). This was clearly written and justified in the text, lines 227 or 303 of the initial manuscript. Also, this may have led to identify (a) specific isoform(s), including splicing variants as initially addressed.

As the Reviewers will see, while performing the revision of our work, we now have been able to point at a specific isoform of Pard3, namely Pard3ba, whose mRNA expression level, in aortic cells and at the single cell resolution, is uniquely and specifically enhanced in cells contacting emergence ‘hot spots’. Using our Runx1 mutant fish line (dt-Runx1), we also show that expression of Pard3ba mRNAs, in these specific aortic regions, is sensitive to interference with Runx1 activity (i.e dt-Runx1 increases Pard3ba expression). Altogether, our new results strongly support our idea, initially proposed, on the regulation of polarity features during EHT; they indicates intercellular coordination, throughout cooperative cross-talk between aortic and HE/EHT cells. This is compatible with the idea of a ‘tuning’ of apico-basal polarity during the entire EHT time-window (including maturation of the HE to become competent for emergence and the emergence process per se whose morphodynamic complexity relies on regulating apico-basal polarity associated functions (ex: for controlling the specific junctional recycling modes of EHT pol+ and EHT pol- cells, as we suggest using JAM proteins that we have chosen owing to their function in the recruitment of Pard3 proteins for apico-basal polarity establishment)). This complements nicely our work and highlights the relevance of studying the interplay between aortic and HE/EHT cells (which we have started to dissect in the second part of our manuscript). Further work is obviously required to address local, dynamic variations of mRNAs encoding for this specific isoform of Pard3 as well as specific interference with its functions at the spatial and temporal levels (hence on live tissues), which is far beyond the scope of our currently submitted work.

Finally, this emphasizes the importance of the aortic context, at the mesoscopic level, in the regulation of the EHT.

Third, based on these major points and Reviewers suggestions, we propose to take into account the fact that the heterogeneity in emergence morphodynamics was not highlighted and propose the following title:

‘Tuning apicobasal polarity and junctional recycling in the hemogenic endothelium orchestrates the morphodynamic complexity of emerging pre-hematopoietic stem cells’

Regarding Results and Figures, the previous Figures 3 and 4 have been entirely revised, with the support of Supplement Figures (3 and 4 supplement figures, respectively as well as a supplement video to Figure 3). Supplement Figures have also been included to the revised version, for nearly all results that appeared as data not shown (Figure 1 – figure supplement 2: illustrating the maintenance of EHT pol+ and EHT pol- cells after division; Figure 1 – figure supplement 3: illustrating the expression of the hematopoietic marker CD41 by EHT pol+ and EHT pol- cells). Also, a new supplemental figure, Figure 7 – figure supplement 7, has been added to substantiate the impact of interfering with ArhGEF11/PDZ-RhoGEF alternative splicing on hematopoiesis. Finally, a Figure for the Reviewers is added at the end of this file that shows that virtually 100% of aortic floor cells that we consider as hemogenic cells are positive for the hematopoietic marker Gata2b which is upstream of Runx1 (using RNAscope which allows achieving cellular resolution unambiguously).

Reviewer #1 (Public Review):

Summary:

In this research article, the authors utilized the zebrafish embryo to explore the idea that two different cell types emerge with different morphodynamics from the floor of the dorsal aorta based on their apicobasal polarity establishment. The hypothesis that the apical-luminal polarity of the membrane could be maintained after EHT and confer different functionality to the cell is exciting, however, this could not be established. There is a general lack of data supporting several of the main statements and conclusions. In addition, the manuscript is difficult to follow and needs refinement. We present below some questions and suggestions with the goal of guiding the authors to improve the manuscript and solidify their findings.

Here, we wish to emphasize that we do not make the hypothesis that ‘…the apical-luminal polarity of the membrane could be maintained after EHT …’ but that the apico-basal polarity establishment/maintenance controls the type of emergence and their associated cell biological features (EHT pol+ and EHT pol- cellular morphodynamics, establishment of membrane domains). Hence, our work suggests that these emergence modes, as a consequence of their intrinsic characteristics and differences, might have an impact on cellular behavior after the release (to place the work in the broader context of hematopoietic cell fate and differentiation). More specifically, the difference in the biological features of the luminal versus abluminal membrane for the two EHT types (ex: membrane signaling territories, membrane pools devoted to specific functions), might endow the cells with specific functional properties, after the release. What happens to those cells thereafter, except for illustrating the evolution of the luminal membrane for pol+ EHT cells, is beyond the scope of this paper. Here, we analyze and characterize some of the cell biological features of the EHT process per se (the emergence from the aortic floor), including the dynamic interface with adjoining endothelial cells.

Strengths:

New transgenic zebrafish lines developed. Challenging imaging.

Weaknesses:

(1) The authors conclude that the truncated version of Podxl2 fused to a fluorophore is enriched within the apical site of the cell. However, based on the images provided, an alternative interpretation is that the portion of the membrane within the apical side is less stretched than in the luminal side, and therefore the fluorophore is more concentrated and easier to identify by confocal. This alternative interpretation is also supported by data presented later in the paper where the authors demonstrate that the early HE is not polarized (membranes are not under tension and stretched yet). Could the authors confirm their interpretation with a different technique/marker like TEM?

The argument of the apparent enrichment, or exclusion, of a marker depending on membrane stretching (and hence molecular packing) would be valid for any type of molecule embedded in these membranes, including of course endogenous ones (this is one of the general biophysical principles leading to the establishment of membrane domains, structurally and functionally speaking); hence, using another marker would not solve the issue because it would depends on its behavior in regard to packing (in particular lipid packing), which is difficult to anticipate and is a topic in its own (especially in this system that has been poorly investigated in regard to its biophysical and biochemical properties in vivo (including its exposure to the hemodynamics)).

If we follow the logic of the Reviewer, it appears that it is not consistent with our results on the maturing HE. Indeed, in our dt-Runx1 mutants, mKate2-podxl2 is enriched at the luminal membrane of HE cells (HE cells are elongated, and the two membrane domains have a relative equal surface and bending); in comparison, HE cells have the same morphology in control animals than in mutants but, in controls, eGFP-podxl2 and mKate2-podxl2 are equally partitioned between the luminal and abluminal membranes (see Figure 3 – figure supplement 2 (for mKate2-podxl2) and Figure 2 – figure supplement 1 and 2 (for eGFP-podxl2)). In addition, we took care while designing the eGFP and mKate2 fusions to keep the natural podxl2 sequence containing critical cysteine residues to maintain assembly properties and distance from the transmembrane segment (hence the fluorescent protein per se is not directly exposed to membrane stretching).

Finally, electron microscopy is not the approach to use for this issue because requiring tissue fixation which is always at risk because modifying significantly membrane properties. On this line, when we fix embryos (and hence membranes, see our new Figure 4 and its Supplemental Figures), we do not appear to maintain obvious EHT pol+ and pol- cell shapes. In addition, to be conclusive, the work would require not TEM but immuno-EM to be able to visualize the marker(s), which is another challenge with this system.

(2) Could the authors confirm that the engulfed membranes are vacuoles as they claimed, using, for example, TEM? Why is it concluded that "these vacuoles appear to emanate from the abluminal membrane (facing the sub-aortic space) and not from the lumen?" This is not clear from the data presented.

The same argument regarding electron microscopy mentioned on the point before is valid here (in addition, it would require serial sectioning in the case it would be technically feasible to make sure not to miss the very tinny connection that may only suggest ultimate narrowing down of the facing adjacent bilayers, which is quite challenging). The term vacuole which we use with caution (in fact, more often, we use the term pseudo-vacuoles in the initial manuscript, lines 140, 146, 1467 (legend to Figure 1 – figure supplemental 1 or apparent vacuole-like in the same legend lines 1465 and 1476) is legitimate here because we cannot say that they are portions of the invaginated luminal membrane as we could be accused not to show that these membranes are still connected to the luminal surface; we are here at the limit of the resolution that in vivo imaging is allowing for the moment with this system, and we drive the attention of the Reviewer on the fact that we are reaching here a sub-cellular level which is already a challenge by itself.

In addition, if there would not be at some point vacuoles (or pseudo-vacuoles) formed in this system (membrane-bounded organelles), it would be difficult to conceive how, after release of the cell, the fluid inherited from the artic lumen would efficiently be chased from these membranes/organelles (see also our model Figure 1 – figure Supplement 1B).

Why is it concluded that "these vacuoles appear to emanate from the abluminal membrane (facing the sub-aortic space) and not from the lumen?" This is not clear from the data presented.

This is not referring to our data but to the Sato et al 2023 work. For EHT undergoing cells leading to aortic clusters in mammals and avians, vacuolar structures indeed appear to emanate from the ab-luminal side facing the sub-aortic space (we cannot call it basal because we do not know the polarity status of these cells). In the Revised version of the manuscript, we have moved this paragraph referring to the Sato et al work to the Discussion, which gives the possibility to expand a bit on this issue, for more clarity (see the second paragraph of our new Discussion).

(3) It is unclear why the authors conclude that "their dynamics appears to depend on the activity of aquaporins and it is very possible that aquaporins are active in zebrafish too, although rather in EHT cells late in their emergence and/or in post-EHT cells, for water chase and vacuolar regression as proposed in our model (Figure 1 - figure supplement 1B)." In our opinion, these figures do not confirm this statement.

This part of the text has been upgraded and moved to the Discussion (see our answer to point 2), to take Reviewers concern about clarity of the Results text section and allowing elaborating a bit more on this issue. We only wished to drive the attention on the described presence of intracellular vacuolar structures recently addressed in the Sato el al 2023 paper showing EHTcell vacuoles that are proposed to contribute to cellular deformation during the emergence. We take this example to rationalize the regression of the vacuolar structures described Figure 1 - figure supplement 1B, which is why we have written ‘… it is very possible that aquaporins are active in zebrafish too’; the first part of the sentence refers to the Sato et al 2023 paper.

(4) Could the authors prove and show data for their conclusions "We observed that both EHT pol+ and EHT pol- cells divide during the emergence"; "both EHT pol+ and EHT pol- cells express reporters driven by the hematopoietic marker CD41 (data not shown), which indicates that they are both endowed with hematopoietic potential"; and "the full recovery of their respective morphodynamic characteristics (not shown)?".

To the new version of our manuscript, we have added new Supplemental information to Figure 1 (two new Supplemental Figures):

• Figure 1 - figure Supplement 2 that illustrates that both EHT pol+ and EHT pol- cells divide during the emergence as well as the maintenance of morphology for both EHT cell types. We wish also to add here that the maintenance of the EHT pol+ morphology is the most critical point, showing that dividing cells in this system do not necessarily lead to EHT pol- cells.

• Figure 1 - figure Supplement 3 that shows that both EHT cell types express CD41.

(5) The authors do not demonstrate the conclusion traced from Fig. 2B. Is there a fusion of the vacuoles to the apical side in the EHT pol+ cells? Do the cells inheriting less vacuoles result in pol- EHT? It looks like the legend for Fig. 2-fig supp is missing.

As said previously, showing fusion here is not technically possible, but indeed, this is the idea, which fits with the images corresponding to timing points 0-90 minutes (Figure 2A), showing (in particular for the right cell) a large pseudo-vacuole whose membrane is heavily enriched with the polarity marker podxl2 (based on fluorescence signal in a membrane-bounded organelle that, based on its curvature radius, should be more under tension then the more convoluted EHT pol+ cell luminal membrane). Also, EHT pol – cells may be born from HE cells that either inherit from less intracellular vesicles after division (or that are derived from HE cells that are less – or not - exposed to polarity-dependent signaling (see our data presented in the new Figure 4 and the new version of the Discussion (see paragraphs ‘Characteristics of the HE and complexity of pre-hematopoietic stem cell emergence’ and ‘Spatially restricted control of Pard3ba mRNAs by Runx1’).

Finally, the cartoon Figure 2B is a hypothetical model, consistent with our data, and that is meant to help the reader to understand the idea extrapolated from images that may not be so easy to interpret for people not working on this system. In legend of Figure 2 that describes this issue in the first version of our manuscript (lines 1241-1243), we were cautious and wrote, in parentheses: ‘note that exocytosis of the large vacuolar structure may have contributed to increase the surface of the apical/luminal membrane (the green asterisk labels the lumen of the EHT pol + cell’.

The legend to Figure 2 – figure supplement 1 is not missing (see lines 1492 – 1499 of the first manuscript). The images of this supplement are not extracted from a time-lapse sequence and show that as early as 30hpf (shortly after the beginning of the EHT time-window – around 28hpf), cells on the aortic floor already exhibit podxl2-containing pseudo-vacuolar structures (which we propose is a prerequisite for HE cell maturation into EHT competent cells; see also Figure 2 – figure supplement 2).

(6) The title of the paper "Tuning apico-basal polarity and junctional recycling in the hemogenic endothelium orchestrates pre-hematopoietic stem cell emergence complexity" could be interpreted as functional heterogeneity within the HSCs, which is not demonstrated in this work. A more conservative title denoting that there are two types of EHT from the DA could avoid misinterpretations and be more appropriate.

There was no ambiguity, throughout our initial manuscript, on what we meant when using the word ‘emergence’; it refers only to the extrusion process from the aortic floor.

Reducing our title only to the 2 types of EHT cells would be very reductionist in regard to our work that also addresses essential aspects of the interplay between hemogenic cells, cells undergoing extrusion (EHT pol+ and pol- cells), and their endothelial neighbors (not to mention what we show in terms of the cell biology for the maturing HE and the regulation of its interface with endothelial cells (evidence for vesicular trafficking, specific regulation of HE-endothelial cell intercalation required for EHT progression etc … ). However, and to take this specific comment into account, we propose a slightly changed title saying that there are emergences differentially characterized by their morphodynamic characteristics:

‘Tuning apicobasal polarity and junctional recycling in the hemogenic endothelium orchestrates the morphodynamic complexity of emerging pre-hematopoietic stem cells’

(7) There are several conclusions not supported by data: "Finally, we have estimated that the ratio between EHT pol+ and EHT pol- cells is of approximately 2/1". "We observed that both EHT pol+ and EHT pol- cells divide during the emergence and remain with their respective morphological characteristics". "We also observed that both EHT pol+ and EHT pol- cells express reporters driven by the hematopoietic marker CD41 (data not shown), which indicates that they are both endowed with hematopoietic potential." These conclusions are key in the paper, and therefore they should be supported by data.

Most of the requests of the Reviewer in this point have already been asked in point 4 and were added to the revised version.

Regarding the EHT pol+/pol- ratio, we will keep the ratio to approximately 2/1. The Reviewer should be aware that quantification of EHT cells is a tricky issue and a source of important variability, as can be assessed by the quantifications that we have been performing (see for example figures in which we compare the dt-Runx1 phenotype with Ctrl). This is inherent to this system, more specifically because the EHT process is asynchronous, ranging from approx. 28 hpf to 3 days post fertilization (we have even observed EHT at 5 dpf). We systematically observed heterogeneity in EHT numbers and EHT types between animals and also between experiments (some days we observe EHTs at 48 hpf, others more around 55 hpf or even later). In addition, emergence also proceeds on the lateral side of the aorta and, while it is relatively easy to identify EHT pol+ cells because of their highly characterized morphology, it is more difficult for EHT pol- cells that can be mistaken to round HE cells preparing for division. In the current revision of our work, we provide additional facts and potential explanations on the mechanisms that control this asynchrony and the apparent stochasticity of the EHT process (see results of new Figures 3 and 4).

Reviewer #2 (Public Review):

In this study, Torcq and colleagues make careful observations of the cellular morphology of haemogenic endothelium undergoing endothelial to haematopoietic transition (EHT) to become stem cells, using the zebrafish model. To achieve this, they used an extensive array of transgenic lines driving fluorescent markers, markers of apico-basal polarity (podocalixin-FP fusions), or tight junction markers (jamb-FP fusions). The use of the runx truncation to block native Runx1 only in endothelial cells is an elegant tool to achieve something akin to tissuespecific deletion of Runx1. Overall, the imaging data is of excellent quality. They demonstrate that differences in apico-basal polarity are strongly associated with different cellular morphologies of cells undergoing EHT from HE (EHT pol- and EHT pol+) which raises the exciting possibility that these morphological differences reflect the heterogeneity of HE (and therefore HSCs) at a very early stage. They then overexpress a truncated form of Runx1 (just the runt domain) to block Runx1 function and show that more HE cells abort EHT and remain associated with the embryonic dorsal aorta. They identify pard3aa and pard3ab as potential regulators of cell polarity. However, despite showing that loss of runx1 function leads to (late) decreases in the expression of these genes, no evidence for their role in EHT is presented. The FRAP experiments and the 2d-cartography, albeit very elegant, are difficult to interpret and not very clearly described throughout the text, making interpretation difficult for someone less familiar with the techniques. Finally, while it is clear that ArhGEF11 is playing an important role in defining cell shapes and junctions between cells during EHT, there is very little statistical evidence to support the limited data presented in the (very beautiful) images.

As mentioned in the response to reviewer 1, we revised our whole strategy for the analysis of the role of Pard3 proteins in regulating the emergence of hematopoietic precursors. Our new data, obtained using refined gene expression analysis by qRT-PCR on FACS sorted populations and by in situ gene expression analysis at the single-cell resolution using RNAscope, show first that a unique Pard3 isoform (Pard3ba) is sensitive to runx1 activity, and that its expression is specifically localized in aortic cells contacting hemogenic(HE)/EHT cells. We show a clear correlation between the densification of Pard3ba mRNAs and the presence of contacting HE/EHT cells, suggesting a key role for Pard3ba in a cross talk between aortic and hemogenic cells. Furthermore, we show that our dt-runx1 mutant impacts on the maturation of HE cells; when this mutant is expressed, we observe, in comparison to control, an accumulation of HE cells that are abnormally polarized as well as unusually high numbers of EHT pol+ cells. This strongly suggests that the polarity status of HE cells controls the mode of emergence. Overall, our work shows that regulation of apico-basal polarity features is essential for the maturation of the HE and the proper proceeding of the EHT.

We made efforts to explain more clearly the FRAP experiments as well as the analysis of 2Dcartography throughout the text to facilitate readers comprehension. 2D-cartography are an invaluable tool to precisely discriminate between endothelial and hemogenic cells, and their usage was essential during the FRAP sessions, to point at specific junctional complexes accurately. Performing FRAP at cellular junctions during aortic development was extremely challenging technically and the outcome subjected to quite significant variability (which often leads to quantitative results at the limit of the statistical significance, which is why we speak of tendencies in our results section reporting on this type of experiments). Apart from constant movement and drifting of the embryos which are sources of variability, the EHT process per se is evolving over time and does so at heterogeneous pace (for example, the apical closure of EHT pol+ cells is characterized by a succession of contraction and stabilization phases, see Lancino et al. 2018) which is an additional source of variability in the measurements. Despite all this, our data collectively and consistently suggest a differential regime of junctional dynamics between EHT cell types and support the critical function of ArhGEF11/PDZ-RhoGEF in the control of junctional turnover at the interface between HE and aortic cells as well as between HE cells to regulate cell-cell intercalation.

There is a sense that this work is both overwhelming in terms of the sheer amount of imaging data, and the work behind it to generate all the lines they required, and at the same time that there is very little evidence supporting the assertion that pard3 (and even ArhGEF11) are important mediators of cell morphology and cell fate in the context of EHT. For instance, the pard3 expression data, and levels after blocking runx1 (part of Figure 3 and Figure 4) don't particularly add to the manuscript beyond indicating that the pard3 genes are regulated by Runx1.

We thank the reviewer for the comment on the Pard3 data particularly because it led us to reconsider our strategy to address with more precision and at the cellular resolution the potential function of this protein family during the time-window of the EHT. As summarized in the header of the Public Review, we identified one specific isoform of Pard3 in the zebrafish - Pard3ba – whose sensitivity to runx1 interference and spatial restriction in expression reinforce the idea of a fine control of apico-basal polarity features and associated functions while EHT is proceeding. Our new data also reinforce the interplay between HE/EHT cells and their direct endothelial neighbors.

Weaknesses

The writing style is quite convoluted and could be simplified for clarity. For example, there is plenty of discussion and speculation throughout the presentation of the results. A clearer separation of the results from this speculation/discussion would help with understanding. Figures are frequently presented out of order in the text; modifying the figures to accommodate the flow of the text (or the other way around) - would make it much easier to follow the narrative. While the evidence for the different cellular morphologies of cells undergoing EHT is strong, the main claim (or at least the title of the manuscript) that tuning apico-basal polarity and junctional recycling orchestrate stem cell emergence complexity is not well supported by the data.

We refined our text when necessary, in particular taking care of transferring and substantiating the arguments that appeared in the Results section, to the Discussion. We also made efforts, on several occasions and for clarity, to describe more precisely the results presented in the different panels of the Figures.

As mentioned in the header of the text of the Public Review and the response to the 6th point of the Public Review of Reviewer 1, we modified slightly the title to avoid ambiguity. In addition, we added a new paragraph to the beginning of our discussion that summarizes the impact of our findings and, we believe, legitimates our title.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Embryonic stages should be indicated in all images presented for clarification.

We thank the reviewer for this point, we added stages when missing on the figures (Figure 1, Figure 1 - Figure supplement 1, Figure 2, Figure 2 - Figure supplement 1, Figure 5, Figure 6, Figure 6 - Figure supplement 1, Figure 7 - Figure supplement 3, Figure 7 - Figure supplement 5, Figure 7 - Figure supplement 6)

(2) In which anatomical site/s were images from Fig 1C and D taken? The surrounding environment looks different, for example, cells in Fig1D seem to be surrounded by other cells, resembling the endothelial plexus at the CHT, while the cells in Fig. 1C seem to be in the dorsal aorta. Is there a spatial difference depending on where cells are budding off? The authors state that there are no differences, but no quantification or data demonstrating that statement is provided.

As mentioned in the figure legend (lines 1206-1209 of the original manuscript), images for Figure 1C and 1D were both taken at the boundary between the end of the AGM and the entry in the caudal hematopoietic tissue. As the images were acquired from different embryos, the labelling of the underlying vein differs between the two panels, with veinous tissues being more sparsely labelled in panel C than in panel D. These images were chosen to illustrate the clearly opposite morphology between the two EHT types that we describe. However, for the rest of the paper, all images and all analysis were exclusively acquired / performed in the dorsal aorta in the AGM, in a region spanning over approximately 10-12 inter-segmentary vessels, starting from the end of the elongated yolk up to the start of the balled yolk. In light of the work from the lab of Zilong Wen showing that only cells emerging anteriorly exhibit long-term replenishment potential (Tian et al. 2017), we specifically chose to limit our comparative analysis to the AGM region and did not quantitatively investigate emergences occurring in the caudal region of the aorta. Additionally, although we routinely observe both types of emergences occurring in the caudal region of the dorsal aorta, we did not quantify the frequency of either EHT events in this region.

Finally, the EHT pol+ cells that we show Figure 1C are of the highest quality obtained ever; one reason is that these two cells emerge at the entry of the CHT which is a region a lot easier to image at high resolution in comparison to the trunk because the sample is less thick and because we are less perturbed by heart beats.

(3) Which figure shows "EHT pol- cells were observed in all other Tg fish lines that we are routinely imaging, including the Tg(Kdrl:Gal4;UAS:RFP) parental line that was used for transgenesis, thus excluding the possibility that these cells result from an artefact due to the expression of a deleted form of Podxl2 and/or to its overexpression."? It would be informative to include this figure.

Other examples of EHT pol- cells were shown Figure 5C as well as Figure 6B using the Tg(kdrl:Jam3b-eGFP; kdrl:nls-mKate2) fish line, that was routinely used for junctional dynamic analyses by FRAP. Furthermore, we add now a new figure (New Figure 1 – figure supplement 3), to illustrate the presence of EHT pol- cells using the Tg(CD41:eGFP) transgenic background, additionally illustrating that EHT pol- cells are CD41 positive.

(4) Are the spinning disk confocal images a single plane? Or maximum projections? Sometimes this is not specified.

We made sure to take into account this remark and went through all figures legends to specify the type of images presented (Figure 1 – figure supplement 1, Figure 2, Figure 2 – figure supplement 1, Figure 2 – figure supplement 2, Figure 7 – figure supplement 3) and also, when relevant, we added this information directly to the figure panels (Figure 6A – 6B).

(5) Could the expression data by RT-qPCR for the Pard3 isoforms be shown? Additionally, it would be appreciated if this expression data could be complemented using Daniocell (https://daniocell.nichd.nih.gov/).

As mentioned in the first paragraph of our response to Public Reviews, and based on reviewers’ comments, we revised our strategy for the investigation of pard3 proteins expression in the vascular system, for their potential role in EHT and sensitivity to runx1. First, we used FACS sorting as well as tissue dissection to enrich in aortic endothelial cells and perform our qPCR analyses (see the new Figure 4 – figure supplement 1A and Figure 4 – figure supplement 3A for the strategy). As asked by the reviewers and for more transparency, we show the expression relative to the housekeeping gene ef1a in our different control samples (new Figure 4 – figure supplement 1C). Furthermore, we used single-molecule FISH to precisely characterise in situ the expression of several of the Pard3 isoforms (Pard3aa, Pard3ab and Pard3ba, which, based on qPCR, were the most relevant for our investigation in the vascular system) (see lines 386 to 412 in text relative to Figure 4 – figure supplement 2). This new addition nicely shows the different pattern of expression of 3 of the Pard3 zebrafish isoforms in the trunk of 2dpf embryos, outlining interesting specificities of each isoform expression in different tissues.

We thank the reviewer for this suggestion to complement our data with the published Daniocell dataset. However, and potentially due to the poor annotation of the different pard3 genes on public databases, gene expression information was absent for two of our isoforms of interest (pard3aa and pard3ba), that we ultimately show to be the most enriched in the vascular system in the trunk. Daniocell gene expression data for the Pard3ab isoform at 48hpf show expression in pronephric duct at 48-58hpf, as well as in intestine progenitors and neuronal progenitors, which is consistent with our in situ observations using RNAscope. However, pard3ab is poorly detected within the hematopoietic and vascular clusters. This observation is coherent with our data that do not show any enrichment of this isoform in vascular tissues compared to other structures. On the other hand, pard3bb does not seem to be particularly enriched in vascular/hematopoietic clusters at 48-58hpf in the Daniocell dataset, in accordance to what we observe with our qPCR. Finally, in the Daniocell dataset, all of the pard3 variants (pard3ab, pard3bb, PARD3 and PARD3 (1 of many)) seem to be either scarcely or not detected in the hematopoietic/vascular system. In our case, for all the isoforms we studied in control condition (pard3aa, pard3ab and pard3ba), and although the technic is only semi-quantitative due to the presence of an amplification step, RNAscope assays seem to indicate a very low expression in aortic cell (with sometime as little as one mRNA copy per cell; this explains low detection in single-cell RNAseq datasets and is coherent with the Daniocell dataset.

(6) It would be informative to add in the introduction some information on apico-basal polarity, tight junctions, JAMs (ArhGEF11/PDZ-RhoGEF).

We modified the introduction so as to add relevant information on Pard3 proteins, their link with our JAMs reporters in the context of polarity establishment, as well as the role of ArhGEF11/PDZ-RhoGEF and its alternative splicing variants in regulating junctional integrity in the context of epithelial-to-mesenchymal transition (lines 99 to 127). This modification of the introduction also allowed us to lighten some parts of the result section (lines 222 to 224, 345 to 349 and 454 to 456 of the original manuscript).

Reviewer #2 (Recommendations For The Authors):

(1) There is lots of data (and lots of work) in this paper; I feel that the pard3 data doesn't substantially add to the paper, and at the same time there is data missing (see point 10, point 11 below for an example).

To add to the clarity and substantiate our findings on Pard3, we revised entirely our investigation strategy as mentioned in previous paragraphs. We refined the characterization of Pard3 isoforms expression in the vascular tissue, using both cell enrichment by FACS for gene expression analysis as well as single-molecule FISH (RNAscope) to access to spatial information on the expression of pard3 isoforms, reaching sub-cellular resolution.

This new strategy allowed us to show the unexpected localization of Pard3ba mRNAs in mRNAs enriched regions in the vicinity of HE/EHT cells (new Figure 4, and paragraph Interfering with Runx1 activity unravels its function in the control of Pard3ba expression and highlights heterogeneous spatial distribution of Pard3ba mRNAs along the aortic axis, see the new manuscript). Overall, the new spatial analysis we performed allowed us to substantiate our findings on Pard3ba and suggests a direct interplay between hemogenic cells and their endothelial aortic neighbors; this interplay supposedly relies on apico-basal polarity features that is at least in part regulated by runx1 in the context of HE maturation and EHT.

(2) Labelling of the figures could be substantially improved. In many instances, the text refers to a figure (e.g. Fig 6A), but it has several panels that are not well annotated (in the case of Fig 6A, four panels) or labelled sparsely in a way that makes it easy to follow the text and identify the correct panel in the figure. Even supplementary figures are sparsely labelled. Labelling to include embryonic stages, which transgenic is being used, etc should be added to the panels to improve clarity for the reader.

We revised the figures to added relevant information, including stages, types of images and annotations to facilitate the comprehension, including Figure 6A – 6B, Figure 5B – 5C (see response to Reviewer 1, first comment, for a more complete list of all revised figures, transgenic fish lines and embryonic stages annotations). Furthermore, we revised the integrality of the manuscript to fit as much as possible to the figures and added some annotations to more easily link the text to the figures and panels.

(3) The current numbering of supplementary figures is quite confusing to follow.

We revised the manuscript so as to make sure all principal and supplementary figures were called in the right order and that supplementary figures appearance was coherent with the unfolding of the text. For Figure 7 only, the majority of the supplemental figures are called before the principal figure, as they relate to our experimental strategy that we comment on before describing the results.

(4) Graphs in Fig 4, Fig 7 supplement 1 and some of the supplementary figures miss statistical info for some comparison (I assume when non-significant), and sometimes present a p-value of a statistical test being done between samples across stages - but these are not dealt with in the text. Throughout all graphs, the font size used in graphs for annotation (labelling of samples, x-axis, and in some cases the p values) is very small and difficult to read.

For Figure 7 - figure supplement 1, non-significant p-values of statistical tests were not displayed (as mentioned in the Figure legend, line 1614 of the original manuscript). For the new Figure 4, all p-values are displayed. For new Figure 4 - figure Supplement 1, statistical tests were only performed to compare RFP+ and RFP- cells in the trunk condition (3 biological replicates) and not in the whole embryo condition, for which we did not perform enough replicates for statistical analysis (biological duplicates).

(5) The results are generally very difficult to follow, with a fair amount of discussion included but then very little detail of the experiments per se.

We thank the reviewers for these comments that helped us improve the clarity of the manuscript.

The Results section was revised to move some of the paragraphs to the introduction (see response to Reviewer 1, 6th comment), and some of them to the Discussion (such as lines 149 to 156 or 410 to 416 in the first version of the manuscript referring to vacuolar structures or to the recycling modes of JAMs in EHT pol+ and EHT pol- cells).

(6) The truncated version of runx1 is introduced but its expected effect is not explained until the discussion. Related to this, is it expected that blocking runx1 with this construct (leading to accumulation of cells in the aorta before they undergo EHT) then leads to increased numbers of T-cell progenitors in the thymus? Abe et al (2005, J Immunol) have used the same strategy to overexpress the runt domain in thymocytes and found a decrease in these cells, rather than an increase. Can you explain this apparent discrepancy?

We thank the reviewer for this interesting point on the effect of runx1 interference. This phenotype (increased number of thymic cells) seems to be in agreement with the phenotype that was described in zebrafish using homozygous runx1 mutants (Sood et al. 2010 PMID: 20154212), in which the authors show an increase of lymphoid progenitors in the kidney marrow of adult runx1W84X/W84X mutants compared to controls as well as a similar number of intra-thymic lck:eGFP cells in mutants and controls. Notably, the T-lymphoid lineage seems to be the only lineage spared by the mutation of runx1. This could suggest that in this case either the T-lymphoid lineage can develop independently of runx1 or that a compensation phenomenon (for example by another protein of the runx family) occurs to rescue the generation of T-lymphocytes.

Although our data shows an impact on T-lymphopoiesis, we do not elucidate the exact mechanism leading to an increased number of thymic cells. In our case, we do not know the half-life of our dt-runx1 protein in newly generated hematopoietic cells when our transgene, expressed under the control of the kdrl vascular promoter, ceases to be produced after emergence. The effect we observe could be direct, due to the presence of our mutant protein after 3 days in thymic cells, or indirect, due to the impact of our mutant on the HE, that could lead to the preferential generation of lymphoid-biased progenitors. Similarly, we do not know whether the cells we observe at this stage in the thymus are generated from long-term HSC or short-term progenitors. Indeed, cell tracing analysis from the lab of Zilong Wen (Tian et al. 2017, see our Ref list) show the simultaneous presence of short-term PBI derived and longterm AGM derived thymic cells at 5dpf. Based on this, we can imagine for example that the sur-numerous cells we observe in the thymus are transient populations that could multiply faster in the absence of definitive populations. Conversely, based on our observation of an accumulation of EHT pol+ events, we can imagine that the EHT pol+ and EHT pol- cells are indeed differentially fated and that EHT pol+ may be biased toward a lymphoid lineage. We also know that at the stage we observe (5dpf), RNAscope assay of runx1 show that a vast majority of thymic cells do not express runx1 (our preliminary data), suggesting that the effect we observe would be an indirect one caused by upstream events rather than by direct interference with the endogenous expression of runx1 in thymic cells.

The article referred to by the reviewer (Sato et al. 2005, PMID: 16177090) investigates on the role of runx1 during TCR selection for thymic cell maturation and shows that runx1 signaling lowers the apoptotic sensitivity of double-positive thymocytes when artificially activated, leading to a reduced number of single-positive thymic cells. Furthermore, this paper references another study from the same lab (Hayashi et al. 2000, PMID: 11120804) that used the same strategy to study the role of runx1 on the positive and negative selection steps of T lymphocytes maturation. This paper, although showing that runx1 is important for later stages of T lymphocytes differentiation — the double-positive to single-positive stage maturation —, also shows a relative increase in the amount of double-negative and double-positive thymocytes, that could be coherent with our observations. Indeed, in our case, although we show an increased number of thymic cells, we do not know the relative proportion of the different thymocyte subsets. We could explain the increased number of thymic cells by increased number of DN/DP thymocytes that would not preclude a decrease in single-positive thymocytes. Finally, the cells we observe in the thymus of our dt-runx1 mutants may also be different lymphoid populations, namely ILCs, that would react differently to runx1 interference.

(7) Lines 154-155 refer to aquaporins but are missing a reference. This is a bit of speculation right in the results section and I struggled to understand what the point of it was.

To clarify the argument and ease the flow of the text, as suggested by the reviewers, we transferred this paragraph (lines 149 to 156 of the initial manuscript) to the Discussion section lines 763-789). We additionally made sure to add the missing reference (Sato et al. 2023, see our Ref list).

(8) Lines 173-175, indicating that both EHTpol+ and pol- express the CD41 transgenic marker - would be useful to show this data.

We provide a new supplement Figure (Figure 1 – figure supplement 3), where, using an outcross of the CD41:eGFP and kdrl:mKate2-podxl2 transgenic lines, we show unambiguously and for multiple cells that both polarized EHT pol+ cells and non-polarized EHT pol- cells are CD41 positive. In addition, but not commented on in the main text, we can also see that an HE cell, characterized by its elongated morphology (in the middle of the field), its thickened nucleus and its position on the aortic floor, is also CD41 positive.

(9) Lines 181-201 - it's not clear how HE cells were identified in the first place - was it just morphology? Or were they identified retrospectively?

HE cells were identified solely on morphology and spatial criteria (as mentioned in the Methods section, lines 1073-1082 and 1108-1111 of the first manuscript). Furthermore, a recent investigation by the lab of Zilong Wen (Zhao et al. 2022, see our Ref list) questioning the common origin of HE cells and of endothelial cells as well as their respective capacity to extrude from the aorta to generate hematopoietic cells showed, by single-cell tracing, that 96% of floor cells are indeed hemogenic endothelial cells. Furthermore, as mentioned in the response to the 8th point, we show in Figure 1 – figure supplement 3 that all floor cells express CD41. Finally, we also used an alternative method to validate the true hemogenic identity of aortic floor cells and show, using RNAscope, that virtually 100% of floor cells that we consider as typical HE cells are indeed expressing an hematopoietic transcription factor upstream of Runx1, namely Gata2b (see Author response image 1).

Author response image 1.

All cells from the aortic floor, at 48hpf, express the hematopoietic marker Gata2b. 48 hpf Tg(Kdrl:eGFP) fixed embryos were used for RNAscope using a probe designed to detect Gata2b mRNAs. Subsequently, images were taken using spinning disk confocal microscopy. The image in the top panel is a z-projection of the entire aortic volume of one embryo and shows the full portion of the dorsal aorta from the anterior part (left side, at the limit of the balled yolk) down to the urogenital orifice (UGO, right side). The 4 boxes (1 - 4) delineate regions that have been magnified beneath (2X). The 2X images corresponding to each box are z-projections (top views) or z-sections (bottom views). The bottom views allow to visualize the aortic floor and to mark its position on top views). Pink arrows point at HE cells (elongated in the anteroposterior direction) and at EHT cells (ovoid/round cells; EHT pol+ cell morphology is not preserved after fixation and RNAscope; thus, it cannot be distinguished from ovoid/round EHT pol- cells). Pink dots = RNAscope spots of various sizes. The green cells in the subaortic space that are marked by RNAscope spots are newly born hematopoietic stem and progenitor cells (see for example box 1). This embryo is representative of n = 5 embryos treated and imaged.

(1) Line 276 - the difference between the egfp-podxl2 and mKate-podxl2 - could that be due to the fluorophore used? Also, it would be good to label Fig 3 supplement 2 better and to see a control alongside the runt overexpression.

Line 276 does not point at a difference in control conditions between eGFP-podxl2 and mKatepodxl2 (see in new Figure 1 – figure supplement 3, Figure 2 or in new Figure 3 - figure supplement 2 several examples of non-polarized HE cells in control conditions using both fluorophores) but between control and dt-runx1 conditions, both expressing the mKate2podxl2 transgene. Similarly, the new example that we provide now in the CD41 figure (Figure 1 – figure supplement 3) clearly shows that mKate-podxl2 is enriched at the apical/luminal membrane of EHT pol+ cells while no such enrichment is observed for EHT pol- cells. The Reviewer should be informed that EHT cells are not always the most typical in shape, in particular because cells can be squeezed by underlying tissues and for example the vein; or from the luminal side by flow and tensions on the aortic wall because of heart beat (the more we image up in the trunk, the more difficult the imaging and the stability of cell shape during long time-lapse sequences). To also take into account the reviewer’s comments, we added for the new Figure 3 – figure supplement 2A a control condition next to the dt-runx1 condition.

(2) There is no quantitation data on the number of excess EHT pol+ cells in the DA, or in the thymus data (Figs 3 Supp1 and Fig 3 Supp 3). Can you quantify this data? This would better support the claim that tunin apico-basal polarity alters the morphology of the emerging HE cells.

We added quantifications relative to both the emergence process itself, showing the accumulation of HE and EHT pol+ cells (new Figure 3B), and on hematopoiesis per se (new Figure 3 – figure supplement 1). Indeed, we show a diminution in the number of newly generated cmyb+ cells in the sub-aortic space. Furthermore, we improved our quantification of the later phenotype on the thymus (new Figure 3 – figure supplement 3), using improved segmentation methods, that indeed validate the increase number of thymic cells that we described.

(3) The observed changes in pard3 isoforms are just reading out changes in their expression in the runt1 transgenics, rather than demonstrating a role in apico-basal polarity.

We entirely revised our strategy regarding Pard3 expression analyses (see also the text at the beginning of this file, for the Public Review). But we wish to stress on the point that we did not intend initially to show directly a role of Pard3 proteins in controlling apico-basal polarity in the system, we just intended to provide correlative evidence supporting our observations with the polarity marker podxl2 (by interfering with their function, as written in the text, apico-basal polarity - which is essential for aortic lumenization and maintenance -, would have been impaired, blurring interpretations).

During the revision, we obtained the unexpected finding, using RNAscope, that one Pard3 isoform, namely Pard3ba, is the one Pard3 that is expressed non-homogenously along the aortic axis and, in vast majority, by aortic cells and in the direct vicinity of emergence domains of the aortic floor (see the new Figure 4 and Figure 4 – figure supplements 2, 3).

This correlative relation between expression of Pard3ba in aortic endothelial cells neighbouring HE/EHT cells suggests, as we propose, that a cross talk occurs between hemogenic and aortic cells, and that this cross talk relies, at least in part, on the expression of key components of apico-basal polarity and their associated functional features. In addition, we show that junctional recycling differs between both EHT types, based on our observations on the different dynamics in the turnover of JAM molecules, in the two EHT types. As JAM molecules are also required for the recruitment of Pard3, which initiates the establishment of apico-basal polarity, these different dynamics suggest that the control of apico-basal polarity is involved in supporting the morphodynamic complexity of EHT cell types.

(4) There is a Fig 5, Supp 2 that is neither mentioned nor described anywhere in the manuscript.

Figure 5 - figure Supplement 2 is mentioned lines 366-370 of the original manuscript, to describe the initial validation that was performed for our eGFP-JAM constructs in multiple cell types using an ubiquitous heat-shock promoter. We developed our description of this supplemental figure in the new manuscript (lines 504 to 514).

(5) Lines 445-456 - these read like a bit of discussion, not results. There are other similar parts of the results section that also read like a discussion (e.g. 526-533)

Although we decided to keep this paragraph in the Results section, as it justifies the rationale behind the choice of ArhGEF11/PDZ-RhoGEF, we took the reviewers comment into account and, as mentioned in the response to reviewer 1 6th comment, lightened the Results section by transferring some of the paragraphs to the Introduction or Discussion sections.

(6) The description of Fig 7A (from line 505) is missing the stages at which the experiments were performed (also not labelled on the figure).

The stages at which the experiments were performed is stated in the figure legend (line 1366) as well as in the Methods section of the original manuscript (line 1033). We added the information on top of the panels A and B for more clarity.

(7) Some figures have multiple panels (e.g. Fig 7Aa'), so when referred to in the text, it remains unclear which panel is being referred to.

We modified the text so as to refer more clearly to the different panels when mentioned in the text, particularly with regards to Figure 7 and 8 but also for all the other figures.

Author response:

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

eLife assessment

This important study investigates the transcriptional changes in neurons that underlie loss of learning and memory with age in C. elegans, and how cognition is maintained in insulin/IGF-1-like signaling mutants. The presented evidence is convincing, utilizing a cutting-edge method to isolate neurons from worms for genomics that is clearly conveyed with a rigorous experimental approach. Overall, this study supports that older daf-2 worms maintain cognitive function via mechanisms that are unique from younger wild type worms, which will be of interest to neuroscientists and researchers studying ageing.

Thank you, we appreciate the positive comments.

Public Reviews: 

Reviewer #1 (Public Review): 

The authors perform RNA-seq on FACS-isolated neurons from adult worms at days 1 and 8 of adulthood to profile the gene expression changes that occur with cognitive decline. Supporting data are included indicating that by day 7 of adulthood, learning and memory are reduced, indicating that this time point or after represents cognitively aged worms. Neuronal identity genes are reduced in expression within cognitively aged worms, whereas genes involved in proteostasis, transcription/chromatin, and stress response are elevated. A number of specific examples are provided, representing markers of specific neuronal subtypes, and correlating expression changes to the erosion of particular functions (e.g. motor neurons, chemosensory neurons, aversive learning neurons, etc). 

To investigate whether the upregulation of genes in neurons with age is compensatory or deleterious, the authors reduced the expression of a set of three significantly upregulated genes and performed behavioral assays in young adults. In each case, reduction of expression improved memory, consistent with a model in which age-associated increases impair neuronal function. This claim would be bolstered by an experiment elevating the expression of these genes in young neurons, which should reduce the learning index if the hypothesis is correct. 

This is an interesting suggestion. Our long-term goal is to find ways to improve memory, and to better understand the “rules” that might govern changes with age. In this case, were interested in addressing the hypothesis that genes that rise with age must be compensatory, which is a frequently stated theory that is not often tested. Here we showed that knocking down three genes that are upregulated in aged animals improved memory; our results suggest that the wild-type functions of these genes are likely deleterious for learning and memory functions, and further, that their increased expression with age is not a compensatory function. Certainly for future work, it might be interesting to better understand how and why these specific genes have a deleterious function that increases with age, and whether that function is different in younger animals where they are not highly expressed.

The authors then characterize learning and memory in wild-type, daf-2, and daf-2/daf-16 worms with age and find that daf-2 worms have an extended ability to learn for approximately 10 days longer than wild types. This was daf-16 dependent. Memory was extended in daf-2 as well, and strikingly, daf-2;daf-16 had no short-term memory even at day 1. Transcriptomic analysis of FACS-sorted neurons was performed on the three groups at day 8. The authors focus their analysis on daf-2 vs. daf-2;daf-16 and present evidence that daf-2 neurons express a stress-resistance gene program. One question that remains unanswered is how well the N2 and daf-2;daf-16 correlate overall, and are there differences? This may be informative as wild type and daf-2;daf-16 mutants are not phenotypically identical when it comes to memory, and there may be differences that can be detected despite the overlap in the PCA. This analysis could reveal the daf-16 targets involved in memory. 

Re. daf-2;daf-16 vs N2: This is a good suggestion. Our analysis in Fig. S5 showed that the daf-2 vs N2 comparison shows similar results with the daf-2 vs daf-16;daf-2 comparison, but some additional genes are differentially expressed. Interestingly, the daf-2 vs N2 comparison shows that the bZip transcription factors are upregulated in daf-2 compared with N2 worms (Fig. S6f). This may indicate that additional transcription factors are controlled by the daf-2 mutation in the nervous system in addition to the DAF-16/FOXO transcription factor.

Author response image 1.

We also identified the differentially expressed genes in the Day 8 neuronal daf-16;daf-2 to N2 comparison, as the reviewer is asking about. The samples from different genotypes do separate from one another in the PCA plot, indicating there are differences between daf-16,daf-2 and N2 neurons. However, the difference is smaller and there are fewer genes differentially expressed between daf-16;daf-2 and N2: only 38 genes are significantly higher in daf-16;daf-2, and only 53 genes are significantly higher in N2 (log2FC > 0.5, p-adj<0.05). The genes higher in N2 are enriched in endopeptidase inhibitors, and the genes higher in daf-16;daf-2 are not enriched in any gene ontology terms. These results indicate that there are some differences between daf-16;daf-2 and N2 neurons, which correlates with the behavioral differences we see, but the difference is small compared to daf-2 neurons. We have added these data to the paper (Fig. S4e,f); thank you for the suggestion.

The authors tested eight candidate genes that were more highly expressed in daf-2 neurons vs. daf-2;daf-16 and showed that reduction of 2 and 5 of these genes impaired learning and memory, respectively, in daf-2 worms. This finding implicates specific neuronal transcriptional targets of IIS in maintaining cognitive ability in daf-2 with age, which, importantly, are distinct from those in young wild type worms. 

Reviewer #2 (Public Review): 

Weng et al. perform a comprehensive study of gene expression changes in young and old animals, in wild-type and daf-2 insulin receptor mutants, in the whole animal, and specifically in the nervous system. Using this data, they identify gene families that are correlated with neuronal ageing, as well as a distinct set of genes that are upregulated in neurons of aged daf-2 mutants. This is particularly interesting as daf-2 mutants show both extended lifespans and healthier neurons in aged animals, reflected by better learning/memory in older animals compared with wild-type controls. Indeed, the knockdown of several of these upregulated genes resulted in poorer learning and memory. In addition, the authors showed that several genes upregulated during ageing in wild-type neurons also contribute to learning and memory; specifically knockdown of these genes in young animals resulted in improved memory. This indicates that (at least in this small number of cases), genes that show increased transcript levels with age in the nervous system somehow suppress memory, potentially by having damaging effects on neuronal health. 

Finally, from a resource perspective, the neuronal transcriptome provided here will be very useful for C. elegans researchers as it adds to other existing datasets by providing the transcriptome of older animals (animals at day 8 of adulthood) and demonstrating the benefits of performing tissue-specific RNAseq instead of whole-animal sequencing. 

Thank you!

The work presented here is of high quality and the authors present convincing evidence supporting their conclusions.

Thanks!

I only have a few comments/suggestions: 

(1) Do the genes identified to decrease learning/memory capacity in daf-2 animals (Figure 4d/e) also impact neuronal health? daf-2 mutant worms show delayed onset of age-related changes to neuron structure (Tank et al., 2011, J Neurosci). Does knockdown of the genes shown to affect learning also affect neuron structure during ageing, potentially one mechanism through which they modulate learning/memory? 

Thank you for this suggestion, which would be good for a future direction, particularly for genes that might have some relationship to previously-identified cellular structural process. The genes we tested here include dod-24, alh-2, mtl-1, F08H9,4, C44B7.5, hsp-12.3, hsp-12.6, and cpi-1, which are related to stress response, proteolysis inhibitor, metabolic, and innate immunity GO categories, thus associated with stress resistance, proteolysis, lipid metabolism processes; none are obvious choices for morphological effects.

However, it is worth noting that learning and memory decline much faster (Days 4-8) than morphological differences are observed (generally after Day 12-15). Moreover, those morphological differences have been studied primarily in mechanosensory neurons (touch neurons) rather than the chemosensory neurons that are involved in learning and memory, so additional genes may be required for those differences that we were not focusing on in thisi study.

(2) The learning and memory assay data presented in this study uses the butanone olfactory learning paradigm, which is well established by the same group. Have the authors tried other learning assays when testing for learning/memory changes after the knockdown of candidate genes? Depending on the expression pattern of these genes, they may have more or less of an effect on olfactory learning versus for example gustatory or mechanosensory-based learning. 

The reason that we use the butanone olfactory learning paradigm is because it is more similar to learning of information (neutral odorant association with positive cue (food)) – the kind of memory we would like to preserve in humans - rather than a stress-induced memory, such as starvation or pathogenesis-associated aversive learning paradigms, which are more like PTSD. (There is likely to be quite a bit of overlap in mechanism, however, including the role of genes such as magi-1 and casy-1, so it would not be surprising if many of these genes also were required for other learning paradigms.)

(3) I have a comment on the 'compensatory vs dysregulatory' model as stated by the authors on page 7. I understand that this model presents the two main options, but perhaps this is slightly too simplistic: the gene expression that rises during ageing may be detrimental for memory (= dysregulatory), but at the same time may also be beneficial for other physiological roles in other tissues (=compensatory). 

This is a good point, and we made the clarification that in the text: “There may be other scenarios in which a gene with multiple functions may be detrimental for some behaviors but beneficial for other physiological roles.”

Reviewer #3 (Public Review): 

Summary: 

In this manuscript, Weng et al. detect a neuron-specific transcriptome that regulates aging. The authors first profile neuron-specific responses during aging at a time point where a loss in memory function is present. They discover signatures unique to neurons which validate their pipeline and reveal the loss of neuron identity with age. For example, old neurons reduce the expression of genes related to synaptic function and neuropeptide signaling and increase the expression of chromatin regulators, insulin peptides, and glycoproteins. The authors discover the detrimental effect of selected upregulated genes (utx-1, ins-19, and nmgp-1) by knocking them down in the whole body and detecting improvement of short memory functions. They then use their pipeline to test neuronal profiles of long-lived insulin/IGF mutants. They discover that genes related to stress response pathways are upregulated upon longevity (e.g. dod-24, F08H9.4) and that they are required for improved neuron function in long-lived individuals. 

Strengths: 

Overall, the manuscript is well-written, and the experiments are well-described. The authors take great care to explain their reasoning for performing experiments in a specific way and guide the reader through the interpretation of the results, which makes this manuscript an enjoyable and interesting read. Using neuron-specific transcriptomic analysis in aged animals the authors discover novel regulators of learning and memory, which underlines the importance of cell-specific deep sequencing. The time points of the transcriptomic profiling are elegantly chosen, as they coincide with the loss of memory and can be used to specifically reveal gene expression profiles related to neuron function. The authors showcase on the dod-24 example how powerful this approach is. In long-lived insulin/IGF-1 receptor mutants body-wide dod-24 expression differs from neuron-specific profiles. Importantly, the depletion of dod-24 has an opposing effect on lifespan and learning memory. The dataset will provide a useful resource for the C. elegans and aging community. 

Thank you, we do hope people will find the data useful.

Weaknesses: 

While this study nicely describes the neuron-specific profiles, the authors do not test the relevance in a tissue-specific way. It remains unclear if modifying the responses only in neurons has implications for either memory or potentially for lifespan. The authors point to this in the text and refer to tissue-specific datasets. However, it is possible that the tissue-specific profile changes with age. The authors should consider mining publicly available cell-specific aging datasets and performing neuron-specific RNAi to test the functional relevance of the neuron-specific response. This would strengthen the importance of cell-specific profiling.

Thank you for your suggestions. As we have mentioned in the text, our candidate genes are either (1) only expressed in the neurons (alh-2 and F08H9.4), or they are only more highly expressed in daf-2 compared to wild type only in the nervous system (C44B7.5 or dod-24). Thus, the effect we see from knocking down these genes in daf-2 are likely neuron-specific. Additionaly, we performed our assays with neuron-sensitive RNAi strain CQ745: daf-2(e1370) III; vIs69 [pCFJ90(Pmyo-2::mCherry + Punc-119::sid-1)] V. It has been previously shown that neuronal expression of sid-1 decreases non-neuronal RNAi, suggesting that neurons expressing transgenic sid-1(+) served as a sink for dsRNA (Calixto et al., 2010). Thus, this neuron-sensitive RNAi is likely neuron-specific and our results is unlikely from knocking down these genes in non-neuronal tissues. However, we do acknowledge this issue.

To identify the expression pattern of these genes in a more cell-specific way in the adults, we examined the expression of our candidate genes that affected learning and memory, namely dod-24, F08H9.4, C44B7.9, alh-2, and mtl-1, in the Calico database (Roux et al., 2023). From that database, we can see that dod-24 is mainly expressed in the PHC and PVM neurons, and F08H9.4 is largely expressed in various neurons. Both have only slight expression outside the nervous system. C44B7.5 and mtl-1 are more broadly expressed, but C44B7.5 was not found to be differentially expressed in other tissues in daf-2, and mtl-1 only had a slight effect on learning and memory. Perhaps due to their sequencing depth and detection limit, Roux et al. didn’t detect alh-2 expression anywhere in their data.

Thus, the neuron-specific expression and daf-2 differential expression pattern of these genes indicate that the learning and memory improvement in aged daf-2 is unlikely due to neuronal non-autonomous effects.

To better address this concern (that for the genes that we found only expressed in the neurons, the neuron-confined expression may change with age) we examined the expression pattern change of these genes with age. As is shown below, from the Calico database, we can see that the expression in the nervous system persists, and even slightly increases, with age, thus age-related expression pattern change is not a concern to our analysis.

Author response image 2.

Author response image 3.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Most of my comments are in the public section. A few additional recommendations for the authors regarding the formatting/presentation: 

The presentation of Figure S6e-h in the introduction is somewhat confusing and feels out of order. If presented first, it should be S1. Otherwise, discussion of this figure should go at the end of the results section or in the discussion if appropriate. 

Thank you for pointing this out. We have moved the discussion of this figure to the Discussion section.

I do not see Figure S5 described in the text.

Good catch, thank you. We have added the descriptions for Figure S5 in the text.

In general, check the figures, figure legends, and how they are referenced in the text, particularly the supplemental figures and legends.

Minor comments:

There is a typo in the Figure 4 legend: Neuronal IIX should be IIS. 

Thanks for pointing this out. We have corrected it in the text.

Reviewer #2 (Recommendations For The Authors): 

• There are multiple instances throughout the manuscript where there are statements in brackets that provide justification or explanation for some of the approaches used. There is no reason for 'side note' brackets to be used. I suggest removing them and incorporating these statements into the narrative.

Thank you, we have now incorporated these points into the main text.

• Introduction: page 4 "here we RNA-sequenced FACS-isolated neurons" should be "here we performed RNA sequencing on FACS-isolated neurons...".

Thank you, we have changed the text accordingly.

• Figure 2A: I do not understand the legend for this panel "Tissue Query for wild-type genes expressed at higher levels in aged worms show lower nervous system and neuron prediction score." Please clarify.

We have clarified the Figure 2A legend:

(A)  Tissue prediction score for wild-type genes expressed at higher levels in aged worms.

• Page 8: "We previously observed that loss of single genes that play a role in complex behaviors like learning and memory can have a large impact on function 60, unlike the additive roles of longevity-promoting genes 11." - a large impact on what function?

Thank you for noting, we have clarified it in the text accordingly:

“We previously observed that for genes that play a role in complex behaviors like learning and memory, the loss of single genes can have a large impact on these complex behaviors 60, unlike the additive roles of longevity-promoting genes 11.”

• Next line "Therefore, one mechanism by which wild-type worms lose their function with age..." - again, what function?

Thank you for noting this, we have clarified the text to say we refer to the learning and memory functions.

• Page 9: "Thus, daf-2 mutants maintain their higher cognitive quality of life longer than wild-type worms, while daf-16;daf-2 mutants spend their whole lives without memory ability (Figure 3d), in contrast to claims that daf-2 mutants are less healthy than wild-type or daf-16 worms23." - since ref 23 did not perform any learning/memory tests, the definition of 'health' in ref 23 is different to 'cognitive health' as studied here. So the findings in this study are not 'in contrast' to ref 23 but rather add to these findings.

Learning and memory ability is an important function for a healthy individual, thus we would assert that indeed, cognitive health is an important part of the “health” of daf-2 worms. In ref 23, Bansal et al. claim that daf-2 worms are less healthy without assessing their learning and memory ability; their lack of data is an insufficient reason for us to remove our statement, as cognitive health is part of healthspan. Here we find that the “learning span” of daf-2 lasts at least proportionally if not longer than that of wild type. We have also previously shown that daf-2 worms also have longer maximum velocity span with age (Hahm et al., 2015), in direct contrast with Bansal et al.’s claim that daf-2 worms move less well and thus are less healthy – daf-2 worms simply stop sooner when presented with food and switch to feeding, due to their higher odr-10 levels. The Bansal paper continues to be frequently cited as finding that daf-2 mutants are less healthy than wild type, a claim for which we can still find no experimental evidence to support. Therefore, it is important that we make the point that daf-2 worms have extended cognitive health, which is part of health span.

• Page 13: I feel like the sentence "Furthermore, memory maintenance with age might require additional functions that were not previously uncovered in analyses of young animals" is both vague (what functions are referred to?) and a little bit obvious (obvious that age-related changes would not be revealed in analyses of young animals). Perhaps rephrase to make the desired point clearer? 

We have clarified the sentence in the text:

“Furthermore, memory maintenance with age might require additional genes that function in promoting stress resistance and neuronal resilience, which were not previously uncovered in analyses of young animals.”

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary and Strengths:

The ability of Wolbachia to be transmitted horizontally during parasitoid wasp infections is supported by phylogenetic data here and elsewhere. Experimental analyses have shown evidence of wasp-to-wasp transmission during coinfection (eg Huigins et al), host to wasp transmission (eg Heath et al), and mechanical ('dirty needle') transmission from host to host (Ahmed et al). To my knowledge this manuscript provides the first experimental evidence of wasp to host transmission. Given the strong phylogenetic pattern of host-parasitoid Wolbachia sharing, this may be of general importance in explaining the distribution of Wolbachia across arthropods. This is of interest as Wolbachia is extremely common in the natural world and influences many aspects of host biology.

Weaknesses:

The first observation of the manuscript is that the Wolbachia strains in hosts are more closely related to those in their parasitoids. This has been reported on multiple occasions before, dating back to the late 1990s. The introduction cites five such papers (the observation is made in other studies too that could be cited) but then dismisses them by stating "However, without quantitative tests, this observation could simply reflect a bias in research focus." As these studies include carefully collected datasets that were analysed appropriately, I felt this claim of novelty was rather strong. It is unclear why downloading every sequence in GenBank avoids any perceived biases, when presumably the authors are reanalysing the data in these papers.

Thank you for bringing this to our attention. In this study, we downloaded all wsp sequences from GenBank and conducted a systematic analysis. We acknowledge that there could still be a bias in research focus, but a systematic analysis, compared to a limited dataset, may reduce this bias. We agree with the reviewer's point, and we have revised this statement to make it more accurate. Now the new sentence reads: "However, there is still a lack of systematic statistical analyses to support this hypothesis." (Lines 69–70 in the revised manuscript)

I do not doubt the observation that host-parasitoid pairs tend to share related Wolbachia, as it is corroborated by other studies, the effect size is large, and the case study of whitefly is clearcut. It is also novel to do this analysis on such a large dataset. However, the statistical analysis used is incorrect as the observations are pseudo-replicated due to phylogenetic non-independence. When analysing comparative data like this it is essential to correct for the confounding effects of related species tending to be similar due to common ancestry. In this case, it is well-known that this is an issue as it is a repeated observation that related hosts are infected by related Wolbachia. However, the authors treat every pairwise combination of species (nearly a million pairs) as an independent observation. Addressing this issue is made more complex because there are both the host and symbiont trees to consider. The additional analysis in lines 123-124 (including shuffling species pairs) does not explicitly address this issue.

We agree with your point about the non-independence of data due to phylogenetic relationships. In the analysis of species traits, a conventional phylogenetic correction assumes that traits follow a Brownian motion model (Felsenstein, 1985). The variance of the trait values for a species i is given by:

Var[Yi]=σ2Ti,

Where Ti represents the time from the root to the tip for species i. Consequently, the covariance between traits of species i and j is:

Cov[Yij,Yj]=σ²Tii,

where Tij is the time from the root to the most recent common ancestor (MRCA) of species i and j. Linear model analysis incorporates the covariance matrix to correct for the effects of non-independence. Mathematically, this method is equivalent to the independent contrasts approach (Felsenstein, 1985).

In our analysis, we treat the minimum interspecific wsp distance between two species as a trait for the species pair (i, j). Similarly, for any two pairs of species (i, j) and (k, l), we postulate that the covariance between their traits is given by:

Cov[Y_ij,Y_kl]=σ2⋅(T_ik+T_jl),

where Tik denotes the time from the root to the MRCA of species i and k, and Tjl represents the time from the root to the MRCA of species j and l. This covariance matrix is then incorporated into our linear model analysis to account for the effects of phylogenetic non-independence.

However, when extending trait analysis to pairs of species, the computational demands increase substantially. For instance, with a dataset of 1,377 species, forming all possible pairs yields 947,376 unique species combinations. Consequently, constructing a covariance matrix for these pairs would necessitate storing 897,521,285,376 entries, a requirement that far exceeds the memory capabilities of standard computing systems.

To address this, we randomly sampled 1,000 pairs from the total of 947,376 species pairs within the 'Others' category, thereby reducing the computational load without compromising the representativeness of our analysis. Ultimately, even after accounting for phylogenetic correction using covariance, the effect of parasitism remains highly significant (p < 0.0001).

We have added a “Phylogenetic correction” section to Materials and Methods (Lines 392–405 in the revised manuscript). The corresponding results are described on lines 120–121 and in supplementary Note 1. The data and scripts for this analysis are available at https://doi.org/10.6084/m9.figshare.24718119.

REFERENCE

Felsenstein J, 1985. Phylogenies and the comparative method. The American Naturalist, 125(1), 1-15.

The sharing of Wolbachia between whitefly and their parasitoids is very striking, although this has been reported before (eg the authors recently published a paper entitled "Diversity and Phylogenetic Analyses Reveal Horizontal Transmission of Endosymbionts Between Whiteflies and Their Parasitoids"). In Lines 154-164 it is suggested that from the tree the direction of transfer between host and parasitoid can be inferred from the data. This is not obvious to me given the poor resolution of the tree due to low sequence divergence. There are established statistical approaches to test the direction of trait changes on a tree that could have been used (a common approach is to use the software BEAST).

We thank the reviewer for this constructive feedback on our interpretation of Wolbachia transfer between whiteflies and their parasitoids. Inspired by the reviewer's comments, we have now incorporated a trait-based approach, using the taxonomic order of the source species of the wsp gene as a discrete trait for ancestral state reconstruction on the wsp tree. The estimated ancestral trait state for one clade, which clusters wsp sequences from whiteflies and parasitoids, is Hymenoptera, suggesting that within this clade, the direction of Wolbachia transfer may have been from parasitoids to hosts. Conversely, in another clade characterized by the ancestral trait state of Hemiptera, the inferred direction of transfer appears to be from hosts to parasitoids. We have added a “Ancestral state reconstruction” section to Materials and Methods (Lines 406–412 in the revised manuscript). The corresponding results are described on lines 159–163 and 167–168. The data and script for this analysis is available at https://doi.org/10.6084/m9.figshare.24718119.

Reviewer #2 (Public Review):

The paper by Yan et al. aims to provide evidence for horizontal transmission of the intracellular bacterial symbiont Wolbachia from parasitoid wasps to their whitefly hosts. In my opinion, the paper in its current form consists of major flaws.

Weaknesses:

The dogma in the field is that although horizontal transmission events of Wolbachia occur, in most systems they are so rare that the chances of observing them in the lab are very slim.

For the idea of bacteria moving from a parasitoid to its host, the authors have rightfully cited the paper by Hughes, et al. (2001), which presents the main arguments against the possibility of documenting such transmissions. Thus, if the authors want to provide data that contradict the large volume of evidence showing the opposite, they should present a very strong case.

In my opinion, the paper fails to provide such concrete evidence. Moreover, it seems the work presented does not meet the basic scientific standards.

We are grateful for your critical perspective on our work. Nonetheless, we are confident in the credibility of our findings regarding the horizontal transmission of Wolbachia from En. formosa to B. tabaci. Our study has documented this phenomenon through phylogenetic tree analyses, and we have further substantiated our observations with rigorous experiments in both cages and petri dishes. The horizontal transfer of Wolbachia was confirmed via PCR, with the wsp sequences in B. tabaci showing complete concordance with those in En. formosa. Additionally, we utilized FISH, vertical transmission experiments, and phenotypic assays to demonstrate that the transferred Wolbachia could be vertically transmitted and induce significant fitness cost in B. tabaci. All experiments were conducted with strict negative controls and a sufficient number of replicates to ensure reliability, thereby meeting basic scientific standards. The collective evidence we present points to a definitive case of Wolbachia transmission from the parasitoid En. formosa to the whitefly B. tabaci.

My main reservations are:

- I think the distribution pattern of bacteria stained by the probes in the FISH pictures presented in Figure 4 looks very much like Portiera, the primary symbiont found in the bacterium of all whitefly species. In order to make a strong case, the authors need to include Portiera probes along with the Wolbachia ones.

We thank you for your critical evaluation regarding the specificity of FISH in our study. We assure the reliability of our FISH results based on several reasons.

(1) We implemented rigorous negative controls which exhibited no detectable signal, thereby affirming the specificity of our hybridization. (2) The central region of the whitefly nymphs is a typical oviposition site for En. formosa. Post-parasitism, we observed FISH signals around the introduced parasitoid eggs, distinct from bacteriocyte cells which are rich in endosymbionts including Portiera (Fig 3e-f). This observation supports the high specificity of our FISH method. (3) In the G3 whiteflies, we detected the presence of Wolbachia in bacteriocytes in nymphs and at the posterior end of eggs in adult females (Fig. 4). This distribution pattern aligns with previously reported localizations of Wolbachia in B. tabaci (Shi et al., 2016; Skaljac et al., 2013). Furthermore, the distribution of Wolbachia in the whiteflies does indeed exhibit some overlap with that of Portiera (Skaljac et al., 2013; Bing et al., 2014). 4) The primers used in our FISH assays have been widely cited (Heddi et al., 1999) and validated in studies on B. tabaci and other systems (Guo et al., 2018; Hegde et al., 2024; Krafsur et al., 2020; Rasgon et al., 2006; Uribe-Alvarez et al., 2019; Zhao et al., 2013).

Taking all these points into consideration, we stand by the reliability of our FISH results.

REFERENCES

Bing XL, Xia WQ, Gui JD, et al., 2014. Diversity and evolution of the Wolbachia endosymbionts of Bemisia (Hemiptera: Aleyrodidae) whiteflies. Ecol Evol, 4(13):2714-37.

Guo Y, Hoffmann AA, Xu XQ, et al., 2018. Wolbachia-induced apoptosis associated with increased fecundity in Laodelphax striatellus (Hemiptera: Delphacidae). Insect Mol Biol, 27:796-807.

Heddi A, Grenier AM, Khatchadourian C, Charles H, Nardon P, 1999. Four intracellular genomes direct weevil biology: nuclear, mitochondrial, principal endosymbiont, and Wolbachia. Proc Natl Acad Sci USA, 96:6814-6819.

Hegde S, Marriott AE, Pionnier N, et al., 2024. Combinations of the azaquinazoline anti-Wolbachia agent, AWZ1066S, with benzimidazole anthelmintics synergise to mediate sub-seven-day sterilising and curative efficacies in experimental models of filariasis. Front Microbiol, 15:1346068.

Krafsur AM, Ghosh A, Brelsfoard CL, 2020. Phenotypic response of Wolbachia pipientis in a cell-free medium. Microorganisms, 8.

Rasgon JL, Gamston CE, Ren X, 2006. Survival of Wolbachia pipientis in cell-free medium. Appl Environ Microbiol, 72:6934-6937.

Shi P, He Z, Li S, et al., 2016. Wolbachia has two different localization patterns in whitefly Bemisia tabaci AsiaII7 species. PLoS One, 11: e0162558.

Skaljac M, Zanić K, Hrnčić S, et al., 2013. Diversity and localization of bacterial symbionts in three whitefly species (Hemiptera: Aleyrodidae) from the east coast of the Adriatic Sea. Bull Entomol Res, 103(1):48-59.

Uribe-Alvarez C, Chiquete-Félix N, Morales-García L, et al., 2019. Wolbachia pipientis grows in Saccharomyces cerevisiae evoking early death of the host and deregulation of mitochondrial metabolism. MicrobiologyOpen, 8: e00675.

Zhao DX, Zhang XF, Chen DS, Zhang YK, Hong XY, 2013. Wolbachia-host interactions: Host mating patterns affect Wolbachia density dynamics. PLoS One, 8: e66373.

- If I understand the methods correctly, the phylogeny presented in Figure 2a is supposed to be based on a wide search for Wolbachia wsp gene done on the NCBI dataset (p. 348). However, when I checked the origin of some of the sequences used in the tree to show the similarity of Wolbachia between Bemisia tabaci and its parasitoids, I found that most of them were deposited by the authors themselves in the course of the current study (I could not find this mentioned in the text), or originated in a couple of papers that in my opinion should not have been published to begin with.

We appreciate your meticulous examination of the sources for our sequence data. All the sequences included in our phylogenetic analysis were indeed downloaded from the NCBI database as of July 2023. The sequences used to illustrate the similarity of Wolbachia between B. tabaci and its parasitoids include those from our previously published study (Qi et al., 2019), which were sequenced from field samples. Additionally, some sequences were also obtained from other laboratories (Ahmed et al., 2009; Baldo et al., 2006; Van Meer et al., 1999). We acknowledge that in our prior research (Qi et al., 2019), the sequences were directly submitted to NCBI and, regrettably, we did not update the corresponding publication information after the article were published. It is not uncommon for sequences on NCBI, with some never being followed by a published paper (e.g., FJ710487- FJ710511 and JF426137-JF426149), or not having their associated publication details updated post-publication (for instance, sequences MH918776-MH918794 from Qi et al., 2019, and KF017873-KF017878 from Fattah-Hosseini et al., 2018). We recognize that this practice can lead to confusion and apologize for the oversight in our work.

REFERENCES

Ahmed MZ, Shatters RG, Ren SX, Jin GH, Mandour NS, Qiu BL, 2009. Genetic distinctions among the Mediterranean and Chinese populations of Bemisia tabaci Q biotype and their endosymbiont Wolbachia populations. J Appl Entomol, 133:733-741.

Baldo L, Dunning Hotopp JC, Jolley KA, et al., 2006. Multilocus sequence typing system for the endosymbiont Wolbachia pipientis. Appl Environ Microbiol. 72(11):7098-110.

Fattah-Hosseini S, Karimi J, Allahyari H, 2014. Molecular characterization of Iranian Encarsia formosa Gahan populations with natural incidence of Wolbachia infection. J Entomol Res Soc, 20(1):85–100.

Qi LD, Sun JT, Hong XY, Li YX, 2019. Diversity and phylogenetic analyses reveal horizontal transmission of endosymbionts between whiteflies and their parasitoids. J Econ Entomol, 112(2):894-905.

Van Meer MM, Witteveldt J, Stouthamer R, 1999. Phylogeny of the arthropod endosymbiont Wolbachia based on the wsp gene. Insect Mol Biol, 8(3):399-408.

- The authors fail to discuss or even acknowledge a number of published studies that specifically show no horizontal transmission, such as the one claimed to be detected in the study presented.

Thank you for bringing this to our attention. We have made corresponding modifications to the discussion section (Lines 256–271 in the revised manuscript) and have discussed the published studies that report no evidence of horizontal transmission (Lines 260–263 in the revised manuscript). The added sentences read: “Experimental confirmations of Wolbachia horizontal transfer remain relatively rare, with only a limited number of documented cases (24, 27, 37, 38). Additionally, some experiments have found no evidence of horizontal transmission of Wolbachia (39-42).” (Lines 260–263 in the revised manuscript)

Reviewer #3 (Public Review):

This is a very ordinary research paper. The horizontal of endosymbionts, including Wolbachia, Rickettsia etc. has been reported in detail in the last 10 years, and parasitoid vectored as well as plant vectored horizontal transmission is the mainstream of research. For example, Ahmed et al. 2013 PLoS One, 2015 PLoS Pathogens, Chiel et al. 2014 Enviromental Entomology, Ahmed et al. 2016 BMC Evolution Biology, Qi et al. 2019 JEE, Liu et al. 2023 Frontiers in Cellular and Infection Microbiology, all of these reported the parasitoid vectored horizontal transmission of endosymbiont. While Caspi-Fluger et al. 2012 Proc Roy Soc B, Chrostek et al. 2017 Frontiers in Microbiology, Li et al. 2017 ISME Journal, Li et al. 2017 FEMS, Shi et al. 2024 mBio, all of these reported the plant vectored horizontal transmission of endosymbiont. For the effects of endosymbiont on the biology of the host, Ahmed et al. 2015 PLoS Pathogens explained the effects in detail.

Thank you for the insightful comments and for highlighting the relevant literature in the field of horizontal transmission of endosymbionts, including Wolbachia and Rickettsia. After careful consideration of the studies mentioned in the commences, we believe that our work presents significant novel contributions to the field. 1) Regarding the parasitoid-mediated horizontal transmission of Wolbachia, most of the cited articles, such as Ahmed et al. 2013 in PLoS One and Ahmed et al. 2016 in BMC Evolutionary Biology, propose hypotheses but do not provide definitive evidence. The transmission of Wolbachia within the whitefly cryptic species complex (Ahmed et al. 2013) or between moths and butterflies (Ahmed et al. 2016) could be mediated by parasitoids, plants, or other unknown pathways. 2) Chiel et al. 2014 in Environmental Entomology reported “no evidence for horizontal transmission of Wolbachia between and within trophic levels” in their study system. 3) The literature you mentioned about Rickettsia, rather than Wolbachia, indirectly reflects the relative scarcity of evidence for Wolbachia horizontal transmission. For example, the evidence for plant-mediated transmission of Wolbachia remains isolated, with Li et al. 2017 in the ISME Journal being one of the few reports supporting this mode of transmission. 4) While the effects of endosymbionts on their hosts are not the central focus of our study, the effects of transgenerational Wolbachia on whiteflies are primarily demonstrated to confirm the infection of Wolbachia into whiteflies. Furthermore, the effects we report of Wolbachia on whiteflies are notably different from those reported by Ahmed et al. 2015 in PLoS Pathogens, likely due to different whitefly species and Wolbachia strains. 6) More importantly, our study reveals a mechanism of parasitoid-mediated horizontal transmission of Wolbachia that is distinct from the mechanical transmission suggested by Ahmed et al. 2015 in PLoS Pathogens. Their study implies transmission primarily through dirty needle, without Wolbachia infection of the parasitoid, suggesting host-to-host transmission at the same trophic level, where parasitoids serve as phoretic vectors. In contrast, our findings demonstrate transmission from parasitoids to hosts through unsuccessful parasitism, which represents cross-trophic level transmission. To our knowledge, this is the first experimental evidence that Wolbachia can be transmitted from parasitoids to hosts. We believe these clarifications and the novel insights provided by our research contribute valuable knowledge to the field.

REFERENCES

Ahmed MZ, De Barro PJ, Ren SX, Greeff JM, Qiu BL, 2013. Evidence for horizontal transmission of secondary endosymbionts in the Bemisia tabaci cryptic species complex. PLoS One, 8(1):e53084.

Ahmed MZ, Li SJ, Xue X, Yin XJ, Ren SX, Jiggins FM, Greeff JM, Qiu BL, 2015. The intracellular bacterium Wolbachia uses parasitoid wasps as phoretic vectors for efficient horizontal transmission. PLoS Pathog, 10(2):e1004672.

Ahmed MZ, Breinholt JW, Kawahara AY, 2016. Evidence for common horizontal transmission of Wolbachia among butterflies and moths. BMC Evol Biol, 16(1):118.

Caspi-Fluger A, Inbar M, Mozes-Daube N, Katzir N, Portnoy V, Belausov E, Hunter MS, Zchori-Fein E, 2012. Horizontal transmission of the insect symbiont Rickettsia is plant-mediated. Proc Biol Sci, 279(1734):1791-6.

Chiel E, Kelly SE, Harris AM, Gebiola M, Li X, Zchori-Fein E, Hunter MS, 2014. Characteristics, phenotype, and transmission of Wolbachia in the sweet potato whitefly, Bemisia tabaci (Hemiptera: Aleyrodidae), and its parasitoid Eretmocerus sp. nr. emiratus (Hymenoptera: Aphelinidae). Environ Entomol, 43(2):353-62.

Chrostek E, Pelz-Stelinski K, Hurst GDD, Hughes GL, 2017. Horizontal transmission of intracellular insect symbionts via plants. Front Microbiol, 8:2237.

Li SJ, Ahmed MZ, Lv N, Shi PQ, Wang XM, Huang JL, Qiu BL, 2017. Plant-mediated horizontal transmission of Wolbachia between whiteflies. ISME J, 11(4):1019-1028.

Li YH, Ahmed MZ, Li SJ, Lv N, Shi PQ, Chen XS, Qiu BL, 2017. Plant-mediated horizontal transmission of Rickettsia endosymbiont between different whitefly species. FEMS Microbiol Ecol, 93(12).

Liu Y, He ZQ, Wen Q, Peng J, Zhou YT, Mandour N, McKenzie CL, Ahmed MZ, Qiu BL, 2023. Parasitoid-mediated horizontal transmission of Rickettsia between whiteflies. Front Cell Infect Microbiol, 12:1077494.

Qi LD, Sun JT, Hong XY, Li YX, 2019. Diversity and phylogenetic analyses reveal horizontal transmission of endosymbionts between whiteflies and their parasitoids. J Econ Entomol, 112(2):894-905.

Shi PQ, Wang L, Chen XY, Wang K, Wu QJ, Turlings TCJ, Zhang PJ, Qiu BL, 2024. Rickettsia transmission from whitefly to plants benefits herbivore insects but is detrimental to fungal and viral pathogens. mBio, 15(3):e0244823.

Weaknesses:

In the current study, the authors downloaded the MLST or wsp genes from a public database and analyzed the data using other methods, and I think the authors may not be familiar with the research progress in the field of insect symbiont transmission, and the current stage of this manuscript lacking sufficient novelty.

We appreciate your critical perspective on our study. However, we respectfully disagree with the viewpoint that our manuscript lacks sufficient novelty.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The data and scripts from the experimental section of the paper are not made publicly available. This would be good practice. It may well be a requirement for this journal too, but I have not read the journal policy on this matter.

Thank you for the kind reminder, we have uploaded the data and scripts to the public database at https://doi.org/10.6084/m9.figshare.24718119.

• Line 16 should read 'intertrophic' not 'intertropical'.

Corrected.

• Line 50 should not say 'the most infectious' as this is an incorrect use of the word 'infectious'. Maybe 'common'? Should also add something like 'likely' here.

Corrected. The new sentence reads “Together, these characteristics make Wolbachia likely the most common microbe on Earth in terms of the number of species it infects (7, 8).” (Lines 47–49 in the revised manuscript).

• Line 54 These references are all about mosquito disease vectors, not pests. More generally, in this paragraph, the research interest in Wolbachia relates overwhelmingly to blocking arbovirus transmission and not controlling pest populations.

To enhance consistency with our statements, we have revised the supporting references as follows:

X. Zheng et al., "Combined incompatible and sterile insect techniques eliminate mosquitoes," Nature 572, 56-61 (2019).

A. A. Hoffmann et al., "Wolbachia establishment in Aedes populations to suppress dengue transmission," Nature 476, 454-457 (2011).

J. T. Gong, T. P. Li, M. K. Wang, X. Y. Hong, "Prospects of Wolbachia in agricultural Pest Control," Current Opinion in Insect Science 57, 101039 (2023).J. T. Gong et al., "Stable integration of plant-virus-inhibiting Wolbachia into planthoppers for rice protection," Current Biology 30, 4837-4845.e4835 (2020).

Regarding the content of the articles:

Zheng et al. (2019) detail the successful suppression of wild mosquito populations through the release of male mosquitoes artificially infected with Wolbachia.

Gong et al. (2020) present the potential of releasing Wolbachia-infected brown planthoppers to inhibit plant viruses and control pest populations.

Gong et al. (2023) provide a comprehensive review on the application and future of Wolbachia in managing agricultural pests.

• Line 60-61. This sentence seems poorly supported by theory or data. I suggest it is deleted. Why should CI cause extinction, and why would it have a major effect on genetic diversity beyond mtDNA?

We have deleted the statements about extinction or genetic diversity. Now the sentence reads “It may also spread to nontarget organisms, potentially disrupting their population dynamics.” (Lines 57–58 in the revised manuscript)

• Line 66. Reword to make clear these routes are not an exhaustive list.

We have reworded these sentences. The new sentences now read “Similar to other symbionts, Wolbachia host shifts may occur through three main routes: parasitism, predation, and shared plant or other food sources (17). However, it is important to note that these are not the only routes through which transmission may occur, and the specific contributions of each to the overall process of host shift are not yet fully understood.” (Lines 62–66 in the revised manuscript).

• Line 77-79. This could do with mentioning studies of parasitoid-to-host transmission like Ahmedd et al given that it is common knowledge that insects commonly survive parasitoid attacks.

We have added sentences acknowledging the common occurrence of insects surviving parasitoid attacks and referenced and described the Ahmed et al. 2015 study. The added sentences read:

“However, it is common in nature for hosts to survive parasitoid attacks (27-29). For example, whiteflies can survive after attacks of Eretmocerus parasitoids (27). These parasitoids can act as phoretic vectors, facilitating the spread of Wolbachia within whitefly populations through the contamination of their mouthparts and ovipositors with Wolbachia during the probing process (27).” (Lines 77–82 in the revised manuscript).

• Line 173. Mention that there are three replicates of each cage. In Figures 2C and D, it is better to show each replicate as a separate line to see how consistent they are.

In accordance with the reviewer's suggestion, we have included a statement highlighting the replication of our experiments: “Notably, each cage setup was replicated three times to ensure experimental rigor.” (Lines 179–180 in the revised manuscript).

Regarding Figures 2C and D, we have revised the figures to display each replicate as a separate line, as suggested. However, we have encountered a visual clutter that may detract from the clarity of the figures. Additionally, in Figure C, the three black lines, all representing zero values, do not allow for the distinction of individual trends. Therefore, we recommend retaining the original figure format. In accordance with eLife's data policy, we have also provided the source data for all figures, ensuring that readers can access to the detailed data, thus balancing the need for visual simplicity with the provision of comprehensive data.

Author response image 1.

• The GloBI database is central to the phylogenetic analysis and it would be helpful to have a few words in the results stating where this information comes from.

The revised sentence now reads: “To investigate potential horizontal transmission of Wolbachia, we retrieved 4685 wsp sequences from the NCBI database, and species interaction relationships were extracted from the GloBI database (for details, see Methods and Materials).” (Lines 94–96 in the revised manuscript).

Reviewer #3 (Recommendations For The Authors):

To improve the quality of this manuscript, I have some questions and suggestions.

Introduction:

Line 41-42, I don't agree with this statement, as mentioned above, the ways of insect symbiont transmission have been studied in the last 10 years.

According to the reviewer’s suggestion, we have deleted this statement.

Line 75-76, Again, the statement is not correct, many studies have clearly revealed and confirmed that Wolbachia CAN be transferred from parasitoid to their insect hosts including whitefly Bemisia tabaci.

Thank you for your insightful comments. After careful consideration of the studies you have mentioned above, none of these articles provided definitive evidence supporting the transfer of Wolbachia from parasitoids to their insect hosts. A closely related study is Ahmed et al. (2015) in PLoS Pathogens. This article demonstrates that parasitoid wasps can act as phoretic vectors mediating the transmission of Wolbachia between whiteflies. However, Wolbachia did not infect the parasitoid wasps themselves. Therefore, this study does not provide evidence for intertrophic transmission of Wolbachia from parasitoids to their hosts. To avoid confusion, we have cited the Ahmed et al. (2015) reference following this statement and described its findings accordingly. (Lines 88-92 in revised manuscript).

Results:

Line 133-134, Ahmed et al. 2016 BMC Evolution Biology, clearly revealed and confirmed the "common horizontal transmission of Wolbachia between butterflies and moths".

We thank you for guiding us to the relevant study. Ahmed et al. 2016 BMC Evolution Biology suggested common horizontal transmission of Wolbachia between butterflies and moths and proposed that this horizontal transmission might be caused by parasitoid wasps. Here, we present the potential Wolbachia transfer between Trichogramma and their lepidopteran hosts (Lines 135–136 in revised manuscript). Integrating the results from Ahmed et al. 2016, our result also suggests that Trichogramma wasps may be the vectors for horizontal transmission of Wolbachia among lepidopteran hosts. We have discussed this point in the discussion section and cited Ahmed et al. 2016 BMC Evolution Biology (Lines 239–246 in revised manuscript).

Line 176-177, as we know Wolbachia in Encarsia formosa is a strain of parthenogenesis, why did it reduce the female ratio of whitefly progeny after it was transmitted to whitefly B. tabaci, it needs a convincing explanation.

Wolbachia induces parthenogenesis in En. formosa. However, we observed that Wolbachia from En. formosa failed to induce parthenogenesis in B. tabaci, possibly due to the requirement for host gene compatibility. Additionally, we noted a reduced female ratio in B. tabaci infected with En. formosa Wolbachia. We speculate that this might result from the burden imposed by En. formosa Wolbachia on the new host, potentially reducing fertilization success rates and indirectly leading to a decrease in the female ratio. Similarly, we observed a decline in female fecundity, egg hatching rate, and immature survival rate in B. tabaci infected with En. formosa Wolbachia. The mechanisms underlying these fitness costs remain unclear and warrant further in-depth research.

Line 189-190, do the authors have convincing evidence that the 60Gy irradiation only has effects on the reproduction of En. formosa, but does not have any negative effects on the activity of Wolbachia? I think there may be.

We observed that after irradiation, the titer of Wolbachia within En. formosa significantly decreased (Fig S3). We agree that the irradiation may cause other negative effects on Wolbachia which is worth of close investigation. However, even with a significant reduction in Wolbachia titer, irradiation increased the infection rate of Wolbachia in surviving B. tabaci after wasp attacks (Fig 3C). We speculate that this may be due to irradiation of En. formosa increasing the rate of parasitic failure. While the full extent of the effects of irradiation on Wolbachia is not yet clear in our experiments, it does not alter our conclusion that Wolbachia can be transmitted from En. formosa to whitefly hosts through failed parasitism.

Discussion:

Line 289-290, I don't understand, why the authors think from parasitoid Eretmocerus to whitefly, and from Trichogramma to moth, are the same trophic level, they are indeed two different trophic levels.

Thank you for your feedback. We have conducted a thorough search but were unable to locate the specific statement you are referring to. If there has been any ambiguity in our manuscript that has led to confusion, we sincerely apologize for any misunderstanding it may have caused. We agree with your perspective and have always considered the parasitoid Eretmocerus and whitefly, as well as Trichogramma and moth, to be at different trophic levels. However, in the context of specific references, such as Ahmed et al. 2015 in PLoS Pathogens, we believe that Wolbachia is transmitted within the same trophic level without infecting the parasitoid Eretmocerus, merely serving as a phoretic vector to facilitate the spread of Wolbachia among whitefly hosts. Similarly, in the case of Huigens et al. 2000 in Nature, Wolbachia uses lepidopteran hosts as vectors to promote its transmission among Trichogramma without the need to infect the lepidopteran hosts themselves.

Materials and Methods

Line 348, what is tblastn?

We have corrected tblastn to TBLASTN. We are grateful to the reviewer for pointing this out. Here, we utilized TBLASTN instead of BLASTN, to avoid missing the rapidly evolving wsp sequences. Because alignment at the protein level is generally more sensitive than at the nucleotide level. TBLASTN is a bioinformatics tool within the BLAST (Basic Local Alignment Search Tool) suite used for comparing a protein query sequence against a nucleotide database. Specifically, TBLASTN aligns a given protein sequence with nucleotide sequences in a database by translating the nucleotide sequences into all possible protein sequences (considering different reading frames) and comparing them to the query protein sequence.

Line 383, how was the Wolbachia-free line of B. tabaci established, by antibiotics? If so, how do we ensure the antibiotic does not have any negative to other symbionts in whitefly B. tabaci?

The Wolbachia-free line of B. tabaci was collected from field, without the treatment of antibiotics. We have made revisions in the Materials and Methods section to clarify this, stating, "An iso-female line of B. tabaci, which is naturally Wolbachia-free and has not been treated with antibiotics, was established." (Lines 417–418 in the revised manuscript)

Line 419-421 as I mentioned before, the irradiation may have negative effects on Wolbachia too, so change the biology of both Encarsia and whitefly host.

We observed that after irradiation, the titer of Wolbachia within En. formosa significantly decreased (Fig S3). However, even with a significant reduction in Wolbachia titer, irradiation increased the infection rate of Wolbachia in surviving B. tabaci after wasp attacks (Fig 3C). We speculate that this may be due to irradiation of En. formosa increasing the rate of parasitic failure. While the full extent of the effects of irradiation on Wolbachia is not yet clear in our experiments, it does not alter our conclusion that Wolbachia can be transmitted from En. formosa to whitefly hosts through failed parasitism.

Line 452-453, From egg to eclosion, it needs about 21 days to understand suitable temperature and other conditions, during this period, the egg and nymphs can not move, so how to keep the cut-leaf fresh enough in a Petri dish for 21 days?

We apologize for not clearly describing the materials and methods. By using wet cotton to wrap the end of petiole of the leaf, we can keep the leaves fresh for up to a month. We have included this detail in the materials and methods to enhance the reproducibility of the experiment. “A single irradiated wasp was subsequently introduced into a Petri dish, which contained a tomato leaf infested with Wolbachia-free third or fourth instar whitefly nymphs, and wet cotton was used to wrap the end of the leaf petiole to keep the leaf fresh.” (Lines 455–458 in the revised manuscript)

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript describes a series of experiments using human intracranial neural recordings designed to evaluate the processing of self-generated speech in the setting of feedback delays. Specifically, the authors aim to address the question about the relationship between speech-induced suppression and feedback sensitivity in the auditory cortex, whose relationship has been conflicting in the literature. They found a correlation between speech suppression and feedback delay sensitivity, suggesting a common process. Additional controls were done for possible forward suppression/adaptation, as well as controlling for other confounds due to amplification, etc.

Strengths:

The primary strength of the manuscript is the use of human intracranial recording, which is a valuable resource and gives better spatial and temporal resolution than many other approaches. The use of delayed auditory feedback is also novel and has seen less attention than other forms of shifted feedback during vocalization. Analyses are robust, and include demonstrating a scaling of neural activity with the degree of feedback delay, and more robust evidence for error encoding than simply using a single feedback perturbation.

Weaknesses:

Some of the analyses performed differ from those used in past work, which limits the ability to directly compare the results. Notably, past work has compared feedback effects between production and listening, which was not done here. There were also some unusual effects in the data, such as increased activity with no feedback delay when wearing headphones, that the authors attempted to control for with additional experiments, but remain unclear. Confounds by behavioral results of delayed feedback are also unclear.

Overall the work is well done and clearly explained. The manuscript addresses an area of some controversy and does so in a rigorous fashion, namely the correlation between speech-induced suppression and feedback sensitivity (or lack thereof). While the data presented overlaps that collected and used for a previous paper, this is expected given the rare commodity these neural recordings represent. Contrasting these results to previous ones using pitch-shifted feedback should spawn additional discussion and research, including verification of the previous finding, looking at how the brain encodes feedback during speech over multiple acoustic dimensions, and how this information can be used in speech motor control.

We thank the reviewer for their comments and have addressed the concerns point by point in the section “Recommendation for Authors”.

Reviewer #2 (Public Review):

Summary:

"Speech-induced suppression and vocal feedback sensitivity in human cortex", Ozker and colleagues use intracranial EEG to understand audiomotor feedback during speech production using a speech production and delayed auditory feedback task. The purpose of the paper is to understand where and how speaker-induced suppression occurs, and whether this suppression might be related to feedback monitoring. First, they identified sites that showed auditory suppression during speech production using a single-word auditory repetition task and a visual reading task, then observed whether and how these electrodes show sensitivity to auditory feedback using a DAF paradigm. The stimuli were single words played auditorily or shown visually and repeated or read aloud by the participant. Neural data were recorded from regular- and high-density grids from the left and right hemispheres. The main findings were:

• Speaker-induced suppression is strongest in the STG and MTG, and enhancement is generally seen in frontal/motor areas except for small regions of interest in the dorsal sensorimotor cortex and IFG, which can also show suppression.<br /> • Delayed auditory feedback, even when simultaneous, induces larger response amplitudes compared to the typical auditory word repetition and visual reading tasks. The authors presume this may be due to the effort and attention required to perform the DAF task.

• The degree of speaker-induced suppression is correlated with sensitivity to delayed auditory feedback. • pSTG (behind TTS) is more strongly modulated by DAF than mid-anterior STG

Strengths:

Overall, I found the manuscript to be clear, the methodology and statistics to be solid, and the findings mostly quite robust. The large number of participants with high-density coverage over both the left and right lateral hemispheres allows for a greater dissection of the topography of speaker-induced suppression and changes due to audiomotor feedback. The tasks were well-designed and controlled for repetition suppression and other potential caveats.

Weaknesses:

(1) In Figure 1D, it would make more sense to align the results to the onset of articulation rather than the onset of the auditory or visual cue, since the point is to show that the responses during articulation are relatively similar. In this form, the more obvious difference is that there is an auditory response to the auditory stimulus, and none to the visual, which is expected, but not what I think the authors want to convey.

We agree with the reviewer. We have updated Figure 1 accordingly.

(2) The DAF paradigm includes playing auditory feedback at 0, 50, 100, and 200 ms lag, and it is expected that some of these lags are more likely to induce dysfluencies than others. It would be helpful to include some analysis of whether the degree of suppression or enhancement varies by performance on the task, since some participants may find some lags more interfering than others.

We thank the reviewer for this suggestion. In the original analysis, we calculated a Sensitivity Index for each electrode by correlating the high gamma response with the delay condition across trials. To address the reviewer’s question, we now compared delay conditions in pairs (DAF0 vs DAF50, DAF0 vs DAF100, DAF0 vs DAF200, DAF50 vs DAF100, DAF50 vs DAF200 and DAF100 vs DAF200).

Similar to our Suppression Index calculation, where we compared neural response to listening and speaking conditions (Listen-Speak/Listen+Speak), we now calculated the Sensitivity Index by comparing neural response to two delay conditions as follows:

e.g.  Sensitivity Index = (DAF50 – DAF0) / (DAF50 + DAF0). We used the raw high gamma broadband signal power instead of percent signal change to ensure that the Sensitivity Index values varied between -1 to 1.

As shown in the figure below, even when we break down the analysis by feedback delay, we still find a significant association between suppression and sensitivity (except for when we calculate sensitivity indices by comparing DAF50 and DAF100). Strongest correlation (Pearson’s correlation) was found when sensitivity indices were calculated by comparing DAF0 and DAF200.

As the reviewer suggested, participants found DAF200 more interfering than the others and slowed down their speech the most (Articulation duration; DAF0: 0.698, DAF50: 0.726, DAF100: 0.737, and DAF200: 0.749 milliseconds; Ozker, Doyle et al. 2022).

Author response image 1.

(3) Figure 3 shows data from only two electrodes from one patient. An analysis of how amplitude changes as a function of the lag across all of the participants who performed this task would be helpful to see how replicable these patterns of activity are across patients. Is sensitivity to DAF always seen as a change in amplitude, or are there ever changes in latency as well? The analysis in Figure 4 gets at which electrodes are sensitive to DAF but does not give a sense of whether the temporal profile is similar to those shown in Figure 3.

In Figure 4A, electrodes from all participants are color-coded to reflect the correlation between neural response amplitude and auditory feedback delay. A majority of auditory electrodes in the STG exhibit a positive correlation, indicating that response amplitude increases with increasing feedback delays. To demonstrate the replicability of the response patterns in Figure 3, here we show auditory responses averaged across 23 STG electrodes from 6 participants.

Author response image 2.

Response latency in auditory regions also increases with increasing auditory feedback delays. But this delayed auditory response to delayed auditory feedback is expected. In Figure 3, signals were aligned to the perceived auditory feedback onset, therefore we don’t see the latency differences. Below we replotted the same responses by aligning the signal to the onset of articulation. It is now clearer that responses are delayed as the auditory feedback delay increases. This is because participants start speaking at time=0, but they hear their voice with a lag so the response onset in these auditory regions are delayed.

According to models of speech production, when there is a mismatch between expected and perceived auditory feedback, the auditory cortex encodes this mismatch with an enhanced response, reflecting an error signal. Therefore, we referred to changes in response amplitude as a measure of sensitivity to DAF.

(4) While the sensitivity index helps to show whether increasing amounts of feedback delay are correlated with increased response enhancement, it is not sensitive to nonlinear changes as a function of feedback delay, and it is not clear from Figure 3 or 4 whether such relationships exist. A deeper investigation into the response types observed during DAF would help to clarify whether this is truly a linear relationship, dependent on behavioral errors, or something else.

We compared responses to delay conditions in pairs in the analysis presented above (response #2). We hope these new results also clarifies this issue and address the reviewer’s concerns.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major points:

(1) While the correlation between SuppI and SensI is clear here (as opposed to Chang et al), it is unclear if this difference is a byproduct of how SensI was calculated (and not just different tasks). In that paper, the feedback sensitivity was calculated as a metric comparing feedback responses during production and listening, whereas here the SensI is a correlation coefficient during production only. If the data exists, it would be very helpful to also show an analysis similar to that used previously (i.e. comparing DAF effects in both production and playback, either in correlations or just the 200ms delay response). One could imagine that some differences are due to sensory properties, though it is certainly less clear what delay effects would be on listening compared to say pitch shift.

We thank the reviewer for pointing this out. Indeed, the calculation of SensI is different in the two studies. In Chang et al. study, SensI was calculated by comparing perturbed feedback responses during production and passive listening. This is a very meticulous approach as it controls for the acoustic properties of the auditory stimuli under both conditions.

In our study, we didn’t have a passive listening condition. This would require recording the participants’ voice as they were speaking with DAF and playing it back to them in a subsequent passive listening condition. Therefore, we can’t completely eliminate the possibility that some differences are due to sensory properties. However, to address the reviewer’s concern, we examined the voice recordings of 8 participants for acoustic differences. Specifically, we compared voice intensities for different auditory feedback delays (0,50,100 and 200ms) and found no significant differences (F=0, p=0.091).

We think that the difference with the Chang et al. study is an important point to emphasize, therefore we now added in the Discussion:

“In contrast, to replicate this finding in humans, a previous iEEG study by Chang et al. (Chang, Niziolek et al. 2013) used frequency-shifted feedback during vowel production and found that most suppressed auditory sites did not overlap with those sensitive to feedback alterations. Using DAF instead of frequency-shifted feedback, we demonstrated a significant overlap of two neural populations in the STG, along with a strong correlation between the degree of speech-induced suppression and sensitivity to auditory feedback. This discrepancy may be due to different methods of calculating sensitivity to altered feedback. In our study, sensitivity was determined by comparing responses to delayed and non-delayed feedback during production, whereas Chang et al. compared perturbed feedback responses during production and listening. One possibility is that our approach identifies a larger auditory neural population in the STG sensitive to altered feedback. Alternatively, it could indicate a larger population highly sensitive to temporal rather than spectral perturbations in auditory feedback. Thus, we observe a wide overlap of the two neural populations in the STG showing both speech-induced suppression and sensitivity to auditory feedback. Replaying a recording of the participants' own delayed voice back to them, which we were unable to complete in this study, would have made the results of the two studies more comparable while also completely eliminating the possibility of a sensory explanation for the observed response enhancement.”

(2) I am still a bit unclear on how Experiment 4 is different than the no-delay condition in Experiment 3. Please clarify. Also, to be clear, in Experiments 1+2 the subjects were not wearing any headphones and had no additional sidetone?

It is correct that participants were not wearing earphones in Experiments 1&2 (with no additional sidetone), and that they were wearing earphones in Experiments 3&4.

For the “no delay” condition in the DAF experiment (Experiment 3), participants were wearing earphones and reading words with simultaneous auditory feedback. So, this condition was equivalent to visual word reading (Experiment 2), except participants were wearing earphones. Yet, neural responses were much larger for the “no delay” condition in the DAF experiment compared to visual word reading.

We suspected that larger neural responses in the DAF experiment were caused by hearing auditory feedback through earphones. To test and control for this possibility, in a subset of participants, we ran an additional visual word reading experiment (Experiment 4) with earphones and used the same volume settings as in the DAF experiment. We found that response magnitudes were now similar in the two experiments (Experiment 3 and 4) and earphones (with the associated increased sound amplitude) were indeed the reason for larger neural responses. Thus, Experiment 4 differs from the no-delay condition in Experiment 3 only in the stimuli read aloud.

(3) In Figure 3, why is the DAF200 condition activity so much bigger than the other conditions, even prior to the DAF onset? I worry this might bias the rest of the response differences.

In Figure 3B and 3D, time=0 indicates the onset of the perceived auditory feedback. Below we replotted the responses in the same two electrodes but now time=0 indicates the onset of articulation. We see that the peaking time of the responses are delayed as the auditory feedback delay increases. This is because participants start speaking at time=0, but they hear their voice with a lag so the response onset in these auditory regions are delayed. However, like the reviewer pointed out, the response for the DAF200 condition in Electrode G54 is slightly larger even at the very beginning. We think that this small, early response might reflect a response to the bone-conducted auditory feedback, which might be more prominent for the DAF200 condition. Nevertheless, we still see that response amplitude increase with increasing feedback delays in Electrode 63.

(4) Figure 4C, are the labeled recording sites limited to those with significant DAF and/or suppression?

In Figure 4C, we show electrodes that had significant high-gamma broadband responses during all tasks. We write in the Methods: “Electrodes that showed significant response increase (p < 10−4) either before (−0.5 to 0 s) or after speech onset (0 to 0.5 s) with respect to a baseline period (−1 to −0.6 s) and at the same time had a large signal-to-noise ratio (μ/σ > 0.7) during either of these time windows were selected. Electrode selection was first performed for each task separately, then electrodes that were commonly selected were further analyzed.”

(5) Were there any analyses done to control for the effects of vocal changes on the DAF neural responses? The authors' previous paper did note a behavioral effect. This is probably not trivial, as we may not know the 'onset time' of the response, in contrast to pitch shift where it is more regular. If the timing is unknown, one thing that could be tried is to only look early in DAF responses (first 50ms say) to make sure the DAF effects hold.

DAF involves two different perturbations: the absence of feedback at speech onset and the introduction of delayed feedback during playback. The timing of the behavioral effect in response to these two perturbations remains unclear. Aligning the neural responses to the production onset and examining the first 50ms would only capture the response to the acoustic feedback for the no-delay condition within that time window. Conversely, aligning the responses to the playback onset might miss the onset of the behavioral effect, which likely starts earlier as a response to the lack of feedback. We acknowledge the reviewer's point that this is a limitation of the DAF paradigm, and the behavioral effect is not as straightforward as that of pitch perturbation. However, we believe there is no clear solution to this issue.

Minor points:

(1) Figure 3, it might be nice to show the SuppI and SensI on the plots to give the reader a better sense of what those values look like.

We included SuppI and SensI values in the new version of Figure 3.

Reviewer #2 (Recommendations For The Authors):

Minor Comments:

(1) In Figure 1, it is unclear whether the responses shown in B-D correspond to the ROIs shown in Figure A - I am guessing so, but the alignment of the labels makes this slightly unclear, so I suggest these be relabeled somehow for clarity.

This is fixed in the updated version of Figure 1.

(2) In Figure 1D the difference in colors between AWR and VWR is difficult to appreciate - I suggest using two contrasting colors.

This is fixed in the updated version of Figure 1.

(3) Please add y-axis labels for Fig 3B-D. (I believe these are % signal change, but it would be clearer if the label were included).

This is fixed in the updated version of Figure 3.

(4) Can the authors comment on whether the use of speakers for AWR and VWR versus earphones for DAF and VWF- AF may have had an influence on the increased response in this condition? If the AWR were rerun using the headphone setup, or if DAF with 0 ms feedback were run with no other trials including lags, would the large differences in response amplitude be observed?

Participants were not wearing earphones in Experiments 1&2, and that they were wearing earphones in Experiments 3&4.

For the “no delay” condition in the DAF experiment (Experiment 3), participants were wearing earphones and reading words with simultaneous auditory feedback. So, this condition was equivalent to VWR (Experiment 2), except participants were wearing earphones. Yet, neural responses were much larger for the “no delay” condition in the DAF experiment compared to VWR.

Supporting the reviewer’s concerns, we suspected that larger neural responses in the DAF experiment were caused by hearing auditory feedback through earphones. To test and control for this possibility, in a subset of participants, we ran the VWR-AF experiment (Experiment 4) with earphones and used the same volume settings as in the DAF experiment. We found that response magnitudes were now similar in the two experiments (Experiment 3 and 4) and earphones were indeed the reason for larger neural responses.

(5) No data or code were available, I did not see any statement about this nor any github link or OSF link to share their data and/or code.

Data is available in the Github repository: flinkerlab/Sensitivity-Suppression

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

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

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

Weaknesses:

It is essential to notice that m6ADyn does not exactly recapitulate the observed m6A changes. First, this can be due to m6ADyn's limitations. The authors do a great job in the Discussion highlighting these limitations. Indeed, they mention how m6ADyn cannot interpret m6A's implications on nuclear degradation or splicing and cannot model more complex scenario predictions (i.e., a scenario in which m6A both impacts export and degradation) or the contribution of single sites within a gene.

Secondly, since predictions do not exactly recapitulate the observed m6A changes, "active" regulatory events may still play a partial role in regulating m6A changes. The authors themselves highlight situations in which data do not support m6ADyn predictions. Active mechanisms to control m6A degradation levels or mRNA export levels could exist and may still play an essential role.

We are grateful for the reviewer’s appreciation of our findings and their implications, and are in full agreement with the reviewer regarding the limitations of our model, and the discrepancies in some cases - with our experimental measurements, potentially pointing at more complex biology than is captured by m6ADyn. We certainly cannot dismiss the possibility that active mechanisms may play a role in shaping m6A dynamics at some sites, or in some contexts. Our study aims to broaden the discussion in the field, and to introduce the possibility that passive models can explain a substantial extent of the variability observed in m6A levels.

(1) "We next sought to assess whether alternative models could readily predict the positive correlation between m6A and nuclear localization and the negative correlations between m6A and mRNA stability. We assessed how nuclear decay might impact these associations by introducing nuclear decay as an additional rate, δ. We found that both associations were robust to this additional rate (Supplementary Figure 2a-c)."

Based on the data, I would say that model 2 (m6A-dep + nuclear degradation) is better than model 1. The discussion of these findings in the Discussion could help clarify how to interpret this prediction. Is nuclear degradation playing a significant role, more than expected by previous studies?

This is an important point, which we’ve now clarified in the discussion. Including nonspecific nuclear degradation in the m6ADyn framework provides a model that better aligns with the observed data, particularly by mitigating unrealistic predictions such as excessive nuclear accumulation for genes with very low sampled export rates. This adjustment addresses potential artifacts in nuclear abundance and half-life estimations. However, we continued to use the simpler version of m6ADyn for most analyses, as it captures the key dynamics and relationships effectively without introducing additional complexity. While including nuclear degradation enhances the model's robustness, it does not fundamentally alter the primary conclusions or outcomes. This balance allows for a more straightforward interpretation of the results.

(2) The authors classify m6A levels as "low" or "high," and it is unclear how "low" differs from unmethylated mRNAs.

We thank the reviewer for this observation. We analyzed gene methylation levels using the m6A-GI (m6A gene index) metric, which reflects the enrichment of the IP fraction across the entire gene body (CDS + 3UTR). While some genes may have minimal or no methylation, most genes likely exist along a spectrum from low to high methylation levels. Unlike earlier analyses that relied on arbitrary thresholds to classify sites as methylated, GLORI data highlight the presence of many low-stoichiometry sites that are typically overlooked. To capture this spectrum, we binned genes into equal-sized groups based on their m6A-GI values, allowing a more nuanced interpretation of methylation patterns as a continuum rather than a binary or discrete classification (e.g. no- , low- , high methylation).

(3) The authors explore whether m6A changes could be linked with differences in mRNA subcellular localization. They tested this hypothesis by looking at mRNA changes during heat stress, a complex scenario to predict with m6ADyn. According to the collected data, heat shock is not associated with dramatic changes in m6A levels. However, the authors observe a redistribution of m6A mRNAs during the treatment and recovery time, with highly methylated mRNAs getting retained in the nucleus being associated with a shorter half-life, and being transcriptional induced by HSF1. Based on this observation, the authors use m6Adyn to predict the contribution of RNA export, RNA degradation, and RNA transcription to the observed m6A changes. However:

(a) Do the authors have a comparison of m6ADyn predictions based on the assumption that RNA export and RNA transcription may change at the same time?

We thank the reviewer for this point. Under the simple framework of m6ADyn in which RNA transcription and RNA export are independent of each other, the effect of simultaneously modulating two rates is additive. In Author response image 1, we simulate some scenarios wherein we simultaneously modulate two rates. For example, transcriptional upregulation and decreased export during heat shock could reinforce m6A increases, whereas transcriptional downregulation might counteract the effects of reduced export. Note that while production and export can act in similar or opposing directions, the former can only lead to temporary changes in m6A levels but without impacting steady-state levels, whereas the latter (changes in export) can alter steady-state levels. We have clarified this in the manuscript results to better contextualize how these dynamics interact.

Author response image 1.

m6ADyn predictions of m6A gene levels (left) and Nuc to Cyt ratio (right) upon varying perturbations of a sampled gene. The left panel depicts the simulated dynamics of log2-transformed m6A gene levels under varying conditions. The lines represent the following perturbations: (1) export is reduced to 10% (β), (2) production is increased 10-fold (α) while export is reduced to 10% (β), (3) export is reduced to 10% (β) and production is reduced to 10% (α), and (4) export is only decreased for methylated transcripts (β^m6A) to 10%. The right panel shows the corresponding nuclear:cytoplasmic (log2 Nuc:Cyt) ratios for perturbations 1 and 4.

(b) They arbitrarily set the global reduction of export to 10%, but I'm not sure we can completely rule out whether m6A mRNAs have an export rate during heat shock similar to the non-methylated mRNAs. What happens if the authors simulate that the block in export could be preferential for m6A mRNAs only?

We thank the reviewer for this interesting suggestion. While we cannot fully rule out such a scenario, we can identify arguments against it being an exclusive explanation. Specifically, an exclusive reduction in the export rate of methylated transcripts would be expected to increase the relationship between steady-state m6A levels (the ratio of methylated to unmethylated transcripts) and changes in localization, such that genes with higher m6A levels would exhibit a greater relative increase in the nuclear-to-cytoplasmic (Nuc:Cyt) ratio. However, the attached analysis shows only a weak association during heat stress, where genes with higher m6A-GI levels tend to increase just a little more in the Nuc:Cyt ratio, likely due to cytoplasmic depletion. A global reduction of export (β 10%) produces a similar association, while a scenario where only the export of methylated transcripts is reduced (β^m6A 10%) results in a significantly stronger association (Author response image 2). This supports the plausibility of a global export reduction. Additionally, genes with very low methylation levels in control conditions also show a significant increase in the Nuc:Cyt ratio, which is inconsistent with a scenario of preferential export reduction for methylated transcripts (data not shown).

Author response image 2.

Wild-type MEFs m6A-GIs (x-axis) vs. fold change nuclear:cytoplasmic localization heat shock 1.5 h and control (y-axis), Pearson’s correlation indicated (left panel). m6ADyn, rates sampled for 100 genes based on gamma distributions and simulation based on reducing the global export rate (β) to 10% (middle panel). m6ADyn simulation for reducing the export rate for m6A methylated transcripts (β^m6A) to 10% (right panel).

(c) The dramatic increase in the nucleus: cytoplasmic ratio of mRNA upon heat stress may not reflect the overall m6A mRNA distribution upon heat stress. It would be interesting to repeat the same experiment in METTL3 KO cells. Of note, m6A mRNA granules have been observed within 30 minutes of heat shock. Thus, some m6A mRNAs may still be preferentially enriched in these granules for storage rather than being directly degraded. Overall, it would be interesting to understand the authors' position relative to previous studies of m6A during heat stress.

The reviewer suggests that methylation is actively driving localization during heat shock, rather than being passively regulated. To address this question, we have now knocked down WTAP, an essential component of the methylation machinery, and monitored nuclear:cytoplasmic localization over the course of a heat shock response. Even with reduced m6A levels, high PC1 genes exhibit increased nuclear abundance during heat shock. Notably, the dynamics of this trend are altered, with the peak effect delayed from 1.5h heat shock in siCTRL samples to 4 hours in siWTAP samples (Supplementary Figure 4). This finding underscores that m6A is not the primary driver of these mRNA localization changes but rather reflects broader mRNA metabolic shifts during heat shock. These findings have been added as a panel e) to Supplementary Figure 4.

(d) Gene Ontology analysis based on the top 1000 PC1 genes shows an enrichment of GOs involved in post-translational protein modification more than GOs involved in cellular response to stress, which is highlighted by the authors and used as justification to study RNA transcriptional events upon heat shock. How do the authors think that GOs involved in post-translational protein modification may contribute to the observed data?

High PC1 genes exhibit increased methylation and a shift in nuclear-to-cytoplasmic localization during heat stress. While the enriched GO terms for these genes are not exclusively related to stress-response proteins, one could speculate that their nuclear retention reduces translation during heat stress. The heat stress response genes are of particular interest, which are massively transcriptionally induced and display increased methylation. This observation supports m6ADyn predictions that elevated methylation levels in these genes are driven by transcriptional induction rather than solely by decreased export rates.

(e) Additionally, the authors first mention that there is no dramatic change in m6A levels upon heat shock, "subtle quantitative differences were apparent," but then mention a "systematic increase in m6A levels observed in heat stress". It is unclear to which systematic increase they are referring to. Are the authors referring to previous studies? It is confusing in the field what exactly is going on after heat stress. For instance, in some papers, a preferential increase of 5'UTR m6A has been proposed rather than a systematic and general increase.

We thank the reviewer for raising this point. In our manuscript, we sought to emphasize, on the one hand, the fact that m6A profiles are - at first approximation - “constitutive”, as indicated by high Pearson correlations between conditions (Supplementary Figure 4a). On the other hand, we sought to emphasize that the above notwithstanding, subtle quantitative differences are apparent in heat shock, encompassing large numbers of genes, and these differences are coherent with time following heat shock (and in this sense ‘systematic’), rather than randomly fluctuating across time points. Based on our analysis, these changes do not appear to be preferentially enriched at 5′UTR sites but occur more broadly across gene bodies (potentially a slight 3’ bias). A quick analysis of the HSF1-induced heat stress response genes, focusing on their relative enrichment of methylation upon heat shock, shows that the 5'UTR regions exhibit a roughly similar increase in methylation after 1.5 hours of heat stress compared to the rest of the gene body (Author response image 3). A prominent previous publication (Zhou et al. 2015) suggested that m6A levels specifically increase in the 5'UTR of HSPA1A in a YTHDF2- and HSF1-dependent manner, and highlighted the role of 5'UTR m6A methylation in regulating cap-independent translation, our findings do not support a 5'UTR-specific enrichment. However, we do observe that the methylation changes are still HSF1-dependent. Off note, the m6A-GI (m6A gene level) as a metric that captures the m6A enrichment of gene body excluding the 5’UTR, due to an overlap of transcription start site associated m6Am derived signal.

Author response image 3.

Fold change of m6A enrichment (m6A-IP / input) comparing 1.5 h heat shock and control conditions for 5UTR region and the rest of the gene body (CDS and 3UTR) in the 10 HSF! dependent stress response genes.

Reviewer #2 (Public review):

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

We thank the reviewer for the spot-on suggestions and comments on this manuscript.

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

We sincerely thank the reviewer for their thoughtful evaluation and constructive feedback.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Supplementary Figure 5A Data: Please double-check the label of the y-axis and the matching legend.

We corrected this.

(2) A better description of how the nuclear: cytoplasmic fractionation is performed.

We added missing information to the Material & Methods section.

(3) Rec 1hr or Rec 4hr instead of r1 and r4 to indicate the recovery.

For brevity in Figure panels, we have chosen to stick with r1 and r4.

(4) Figure 2D: are hours plotted?

Plotted is the fold change (FC) of the calculated half-lives in hours (right). For the model (left) hours are the fold change of a dimension-less time-unit of the conditions with m6A facilitated degradation vs without. We have now clarified this in the legend.

(5) How many genes do we have in each category? How many genes are you investigating each time?

We thank the reviewer for this question. In all cases where we binned genes, we used equal-sized bins of genes that met the required coverage thresholds. We have reviewed the manuscript to ensure that the number of genes included in each analysis or the specific coverage thresholds used are clearly stated throughout the text.

(6) Simulations on 1000 genes or 2000 genes?

We thank the reviewer for this question and went over the text to correct for cases in which this was not clearly stated.

Reviewer #2 (Recommendations for the authors):

Specific comments:

(1) The manuscript is very clear and well-written. However, some arguments are a bit difficult to understand. It would be helpful to clearly discriminate between active and passive events. For example, in the sentence: "For example, increasing the m6A deposition rate (⍺m6A) results in increased nuclear localization of a transcript, due to the increased cytoplasmic decay to which m6A-containing transcripts are subjected", I would directly write "increased relative nuclear localization" or "apparent increase in nuclear localization".

We thank the reviewer for this careful observation. We have modified the quoted sentence, and also sought to correct additional instances of ambiguity in the text.

Also, it is important to ensure that all relationships are described correctly. For example, in the sentence: "This model recovers the positive association between m6A and nuclear localization but gives rise to a positive association between m6A and decay", I think "decay" should be replaced with "stability". Similarly, the sentence: "Both the decrease in mRNA production rates and the reduction in export are predicted by m6ADyn to result in increasing m6A levels, ..." should it be "Both the increase in mRNA production and..."?

We have corrected this.

This sentence was difficult for me to understand: "Our findings raise the possibility that such changes could, at least in part, also be indirect and be mediated by the redistribution of mRNAs secondary to loss of cytoplasmic m6A-dependent decay." Please consider rephrasing it.

We rephrased this sentence as suggested.

(2) Figure 2d: "A final set of predictions of m6ADyn concerns m6A-dependent decay. m6ADyn predicts that (a) cytoplasmic genes will be more susceptible to increased m6A mediated decay, independent of their m6A levels, and (b) more methylated genes will undergo increased decay, independently of their relative localization (Figure 2d left) ... Strikingly, the experimental data supported the dual, independent impact of m6A levels and localization on mRNA stability (Figure 2d, right)."

I do not understand, either from the text or from the figure, why the authors claim that m6A levels and localization independently affect mRNA stability. It is clear that "cytoplasmic genes will be more susceptible to increased m6A mediated decay", as they always show shorter half-lives (top-to-bottom perspective in Figure 2d). Nonetheless, as I understand it, the effect is not "independent of their m6A levels", as half-lives are clearly the shortest with the highest m6A levels (left-to-right perspective in each row).

The two-dimensional heatmaps allow for exploring conditional independence between conditions. If an effect (in this case delta half-life) is a function of the X axis (in this case m6A levels), continuous increases should be seen going from one column to another. Conversely, if it is a function of the Y axis (in this case localization), a continuous effect should be observed from one row to another. Given that effects are generally observed both across rows and across columns, we concluded that the two act independently. The fact that half-life is shortest when genes are most cytoplasmic and have the highest m6A levels is therefore not necessarily inconsistent with two effects acting independently, but instead interpreted by us as the additive outcome of two independent effects. Having said this, a close inspection of this plot does reveal a very low impact of localization in contexts where m6A levels are very low, which could point at some degree of synergism between m6A levels and localization. We have therefore now revised the text to avoid describing the effects as "independent."

(3) The methods part should be extended. For example, the description of the mRNA half-life estimation is far too short and lacks details. Also, information on the PCA analysis (Figure 4e & f) is completely missing. The code should be made available, at least for the differential model.

We thank the reviewer for this point and expanded the methods section on mRNA stability analysis and PCA. Additionally, we added a supplementary file, providing R code for a basic m6ADyn simulation of m6A depleted to normal conditions (added Source Code 1).

https://docs.google.com/spreadsheets/d/1Wy42QGDEPdfT-OAnmH01Bzq83hWVrYLsjy_B4n CJGFA/edit?usp=sharing

(4) Figure 4e, f: The authors use a PCA analysis to achieve an unbiased ranking of genes based on their m6A level changes. From the present text and figures, it is unclear how this PCA was performed. Besides a description in the methods sections, the authors could show additional evidence that the PCA results in a meaningful clustering and that PC1 indeed captures induced/reduced m6A level changes for high/low-PC1 genes.

We have added passages to the text, hoping to clarify the analysis approach.

(5) In Figure 4i, I was surprised about the m6A dynamics for the HSF1-independent genes, with two clusters of increasing or decreasing m6A levels across the time course. Can the model explain these changes? Since expression does not seem to be systematically altered, are there differences in subcellular localization between the two clusters after heat shock?

A general aspect of our manuscript is attributing changes in m6A levels during heat stress to alterations in mRNA metabolism, such as production or export. As shown in Supplementary Figure 4d, even in WT conditions, m6A level changes are not strictly associated with apparent changes in expression, but we try to show that these are a reflection of the decreased export rate. In the specific context of HSF1-dependent stress response genes, we observe a clear co-occurrence of increased m6A levels with increased expression levels, which we propose to be attributed to enhanced production rates during heat stress. This suggests that transcriptional induction can drive the apparent rise in m6A levels. We try to control this with the HSF1 KO cells, in which the m6A level changes, as the increased production rates are absent for the specific cluster of stress-induced genes, further supporting the role of transcriptional activation in shaping m6A levels for these genes. For HSF1-independent genes, the HSF-KO cells mirror the behavior of WT conditions when looking at 500 highest and lowest PC1 (based on the prior analysis in WT cells), suggesting that changes in m6A levels are primarily driven by altered export rates rather than changes in production.

Among the HSF1 targets, Hspa1a seems to show an inverse behaviour, with the highest methylation in ctrl, even though expression strongly goes up after heat shock. Is this related to the subcellular localization of this particular transcript before and after heat shock?

Upon reviewing the heat stress target genes, we identified an issue with the proper labeling of the gene symbols, which has now been corrected (Figure 4 panel i). The inverse behavior observed for Hspb1 and partially for Hsp90aa1 is not accounted for by the m6ADyn model, and is indeed an interesting exception with respect to all other induced genes. Further investigation will be required to understand the methylation dynamics of Hspb1 during the response to heat stress.

Reviewer #3 (Recommendations for the authors):

Page 4. Indicate reference for "a more recent study finding reduced m6A levels in chromatin-associated RNA.".

We thank the reviewer for this point and added two publications with a very recent one, both showing that chromatin-associated nascent RNA has less m6A methylation

The manuscript is perhaps a bit too long. It took me a long time to get to the end. The findings can be clearly presented in a more concise manner and that will ensure that anyone starting to read will finish it. This is not a weakness, but a hope that the authors can reduce the text.

We have respectfully chosen to maintain the length of the manuscript. The model, its predictions and their relationship to experimental observations are somewhat complex, and we felt that further reduction of the text would come at the expense of clarity.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

This manuscript presents an interesting new framework (VARX) for simultaneously quantifying effective connectivity in brain activity during sensory stimulation and how that brain activity is being driven by that sensory stimulation. The core idea is to combine the Vector Autoregressive model that is often used to infer Granger-causal connectivity in brain data with an encoding model that maps the features of a sensory stimulus to that brain data. The authors do a nice job of explaining the framework. And then they demonstrate its utility through some simulations and some analysis of real intracranial EEG data recorded from subjects as they watched movies. They infer from their analyses that the functional connectivity in these brain recordings is essentially unaltered during movie watching, that accounting for the driving movie stimulus can protect one against misidentifying brain responses to the stimulus as functional connectivity, and that recurrent brain activity enhances and prolongs the putative neural responses to a stimulus.

This manuscript presents an interesting new framework (VARX) for simultaneously quantifying effective connectivity in brain activity during sensory stimulation and how that brain activity is being driven by that sensory stimulation. Overall, I thought this was an interesting manuscript with some rich and intriguing ideas. That said, I had some concerns also - one potentially major - with the inferences drawn by the authors on the analyses that they carried out.

Main comments:

(1) My primary concern with the way the manuscript is written right now relates to the inferences that can be drawn from the framework. In particular, the authors want to assert that, by incorporating an encoding model into their framework, they can do a better job of accounting for correlated stimulus-driven activity in different brain regions, allowing them to get a clearer view of the underlying innate functional connectivity of the brain. Indeed, the authors say that they want to ask "whether, after removing stimulus-induced correlations, the intrinsic dynamic itself is preserved". This seems a very attractive idea indeed. However, it seems to hinge critically on the idea of fitting an encoding model that fully explains all of the stimulus-driven activity. In other words, if one fits an encoding model that only explains some of the stimulus-driven response, then the rest of the stimulus-driven response still remains in the data and will be correlated across brain regions and will appear as functional connectivity in the ongoing brain dynamics - according to this framework. This residual activity would thus be misinterpreted. In the present work, the authors parameterize their stimulus using fixation onsets, film cuts, and the audio envelope. All of these features seem reasonable and valid. However, they surely do not come close to capturing the full richness of the stimuli, and, as such, there is surely a substantial amount of stimulus-driven brain activity that is not being accounted for by their "B" model and that is being absorbed into their "A" model and misinterpreted as intrinsic connectivity. This seems to me to be a major limitation of the framework. Indeed, the authors flag this concern themselves by (briefly) raising the issue in the first paragraph of their caveats section. But I think it warrants much more attention and discussion.

We agree. One can never be sure that all stimulus induced correlation is accounted for. We now formulate our question more cautiously: 

“We will ask here whether, after removing some of the stimulus-induced correlations, the intrinsic dynamic is similar between stimulus and rest conditions.”

We also highlight that one may expect the opposite result of what we found: 

“A general observation of these studies is that a portion of the functional connectivity is preserved between rest and stimulus conditions, while some aspects are altered by the perceptual task [12,16], sometimes showing increased connectivity during the stimulus.[15].” 

We have added a number of additional features (acoustic edges, fixation novelty, and motion) and more carefully characterize how much “connectivity” each one explains in the neural data: 

“Removing any of the input features increased the effect size of recurrent connections compared to a model with all features (Fig. S4). We then cumulatively added each feature to the VARX model. Effect size monotonically decreases with each feature added (Fig. 3F). Decreases of effect size are significant when adding film cuts (ΔR=-3.6*10^-6, p<0.0001, N=26, FDR correction, α=0.05) and the sound envelope (ΔR=-3.59*10^-6, p=0.002, N=26, FDR correction, α=0.05). Thus, adding more input features progressively reduces the strength of recurrent “connections”.”

We also added more data to the analysis comparing movies vs rest. We now use 4 different movie segments instead of 1 and find reduced recurrent connectivity during movies: 

“The number of significant recurrent connections in  were significantly reduced during  movie watching compared to rest (Fig. 4C, fixed effect of stimulus: beta = -3.8*10^-3, t(17) = -3.9, p<0.001), as is the effect size R (Fig. 4D, fixed effect of stimulus: beta = -2.5*10^-4, t(17) = -4.1, p<0.001).”

The additional analysis is described in the Methods section:

“To compare recurrent connectivity between movies and the resting-state, we compute VARX models in four different movie segments of 5 minutes length to match the length of the resting state recording. We use the first and second half of ‘Despicable Me English’, the first half of ‘Inscapes’ and one of the ‘Monkey’ movies. 18 patients include each of these recordings. For each recording in each patient we compute the fraction of significant channels (p<0.001) and average the effect size R across all channel pairs, excluding the diagonal. We test the difference between movies and resting-state with linear mixed-effect models with stimulus as fixed effect (movie vs rest), and patient as random effect, using matlab’s fitlme() routine.”

We had already seen this trend of decreasing connectivity during movie watching before, and reported on it cautiously as “largely unaltered”. We updated the Abstract correspondingly from “largely unaltered” to “reduced”: 

“We also find that the recurrent connectivity during rest is reduced during movie watching.”

We mentioned this possibility in the Discussion before, namely, that additional input features may reduce recurrent connectivity in the model, and therefore show a difference. We discuss this result now as follows: 

“The stimulus features we included in our model capture mostly low-level visual and auditory input. It is possible that regressing out a richer stimulus characterization would have removed additional stimulus-induced correlation. While we do not expect that this would change the overall effect of a reduced number of “connections” during movie watching compared to resting state, the interpretation of changes in specific connections will be affected by the choice of features. For example, in sensory cortices, higher recurrent connectivity in the LFP during rest would be consistent with the more synchronized state we saw in rest, as reflected by larger oscillatory activity. Synchronization in higher-order cortices, however, is expected to be more strongly influenced by semantic content of external input.”

In the Discussion we expand on what might happen if additional stimulus features were to be included into the model:  

“Previous literature does often not distinguish between intrinsic dynamics and extrinsic effects. By factoring out some of the linear effects of the external input we conclude here that recurrent connectivity is reduced in average. From our prior work49, we know that the stimulus features we included here capture a substantial amount of variance across the brain in intracranial EEG. Arguably, however, the video stimuli had rich semantic information that was not captured by the low-level features used here. Adding such semantic features could have further reduced shared variance, and consequently further reduced average recurrent connectivity in the model.”

“Similarities and differences between rest and movie watching conditions reported previously, do not draw a firm conclusion as to whether overall “functional connectivity” is increased or reduced. Results seem to depend on the time scale of neural activity analyzed, and the specific brain networks [12,16,63]. However, in fMRI, the conclusion seems to be that functional connectivity during movies is stronger than during rest[15], which likely results from stimulus induced correlations. The VARX model can remove some of the effects of these stimuli, revealing that average recurrent connectivity may be reduced rather than increased during stimulus processing.”

And in the conclusion we now write: 

“The model revealed a small but significant decrease of recurrent connectivity when watching movies.”

(2) Related to the previous comment, the authors make what seems to me to be a complex and important point on page 6 (of the pdf). Specifically, they say "Note that the extrinsic effects captured with filters B are specific (every stimulus dimension has a specific effect on each brain area), whereas the endogenous dynamic propagates this initial effect to all connected brain areas via matrix A, effectively mixing and adding the responses of all stimulus dimensions. Therefore, this factorization separates stimulus-specific effects from the shared endogenous dynamic." It seems to me that the interpretation of the filter B (which is analogous to the "TRF") for the envelope, say, will be affected by the fact that the matrix A is likely going to be influenced by all sorts of other stimulus features that are not included in the model. In other words, residual stimulus-driven correlations that are captured in A might also distort what is going on in B, perhaps. So, again, I worry about interpreting the framework unless one can guarantee a near-perfect encoding model that can fully account for the stimulus-driven activity. I'd love to hear the authors' thoughts on this. (On this issue - the word "dominates" on page 12 seems very strong.)

This is an interesting point we had not thought about. After some theoretical considerations and some empirical testing we conclude that the effect of missing inputs is relevant, but can be easily anticipated. 

We have added the following to the Results section explaining and demonstrated empirically the effects of adding features and signals to the model: 

“As with conventional linear regression, the estimate in B for a particular input and output channel is not affected by which other signals are included in or , provided those other inputs are uncorrelated. We confirmed this here empirically by removing dimensions from (Fig. S11A), and by adding uncorrelated input to (Fig. S11B, adding fixation onset does not affect the estimate for auditory envelope responses). In other words, to estimate B, we do not require all possible stimulus features and all brain activity to be measured and included in the model. In contrast, B does vary when correlated inputs are added to (Fig. S11C, adding acoustic edges changes the auditory envelope response). Evidently the auditory envelope and acoustic edges are tightly coupled in time, whereas fixation onset is not. When a correlated input is missing (acoustic edges) then the other input (auditory envelope) absorbs the correlated variance, thus capturing the combined response of both.”

(3) Regarding the interpretation of the analysis of connectivity between movies and rest... that concludes that the intrinsic connectivity pattern doesn't really differ. This is interesting. But it seems worth flagging that this analysis doesn't really account for the specific dynamics in the network that could differ quite substantially between movie watching and rest, right? At the moment, it is all correlational. But the dynamics within the network could be very different between stimulation and rest I would have thought.

As discussed above, with more data and additional stimulus features we now see detectable changes in the connectivity. The example in Figure 4G also shows that specific connections may change in different directions, while overall the strength of connections slightly decreases during movie watching compared to rest. We added the following to the results:

“While the effect size decreases on average, there is some variation across different brain areas (Fig. 4E-G).”

But even if the connectivity were unchanged, the activity on this network can be different with varying inputs. We actually also saw that there were changes in the variability of activity (Figs. 6 and S13) that may point to non-linear effects. It seems that injecting the input will cause an overall change in power, which can be explained by a relatively simple non-linear gain adaptation. These effects are already discussed at some length in the paper. 

(4) I didn't really understand the point of comparing the VARX connectivity estimate with the spare-inverse covariance method (Figure 2D). What was the point of this? What is a reader supposed to appreciate from it about the validity or otherwise of the VARX approach?

We added the following motivation and clarification on this topic: 

“To test the descriptive validity [43] of the VARX model we follow the approach of recovering structural connectivity from functional activity in simulation. [44] Specifically, we will compare the recurrent connectivity A derived from brain activity simulated assuming a given structural connectivity, i.e. we ask, can the VARX model recover the underlying structural connectivity, at least in a simulated whole-brian model with known connectivity? … For comparison, we also used the sparse-inverse covariance method to recover connectivity from the correlation matrix (functional connectivity). This method is considered state-of-the-art as it is more sensitive than other methods in detecting structural connections [48]”

(5) I think the VARX model section could have benefitted a bit from putting some dimensions on some of the variables. In particular, I struggled a little to appreciate the dimensionality of A. I am assuming it has to involve both time lags AND electrode channels so that you can infer Granger causality (by including time) between channels. Including a bit more detail on the dimensionality and shape of A might be helpful for others who want to implement the VARX model.

Your assumption is correct. We added the following to make this easier for readers: 

“Therefore, A  has dimensions B has dimensions , where are the dimensions of and respectively.”

(6) A second issue I had with the inferences drawn by the authors was a difficulty in reconciling certain statements in the manuscript. For example, in the abstract, the authors write "We find that the recurrent connectivity during rest is largely unaltered during movie watching." And they also write that "Failing to account for ... exogenous inputs, leads to spurious connections in the intrinsic "connectivity".

Perhaps this segment of the abstract needed more explanation. To enhance clarity we have also changed the ordering of the findings. Hopefully this is more clear now: 

“This model captures the extrinsic effect of the stimulus and separates that from the intrinsic effect of the recurrent brain dynamic. We find that the intrinsic dynamic enhances and prolongs the neural responses to scene cuts, eye movements, and sounds. Failing to account for these extrinsic inputs, leads to spurious recurrent connections that govern the intrinsic dynamic. We also find that the recurrent connectivity during rest is reduced during movie watching.”

Reviewer #2 (Public review):

Summary:

The authors apply the recently developed VARX model, which explicitly models intrinsic dynamics and the effect of extrinsic inputs, to simulated data and intracranial EEG recordings. This method provides a directed method of 'intrinsic connectivity'. They argue this model is better suited to the analysis of task neuroimaging data because it separates the intrinsic and extrinsic activity. They show: that intrinsic connectivity is largely unaltered during a movie-watching task compared to eyes open rest; intrinsic noise is reduced in the task; and there is intrinsic directed connectivity from sensory to higher-order brain areas.

Strengths:

(1) The paper tackles an important issue with an appropriate method.

(2) The authors validated their method on data simulated with a neural mass model.

(3) They use intracranial EEG, which provides a direct measure of neuronal activity.

(4) Code is made publicly available and the paper is written well.

Weaknesses:

It is unclear whether a linear model is adequate to describe brain data. To the author's credit, they discuss this in the manuscript. Also, the model presented still provides a useful and computationally efficient method for studying brain data - no model is 'the truth'.

We fully agree and have nothing much to add to this, except to highlight the benefit of a linear model even as explanation for non-linear phenomena: 

“The [noise-quenching] effect we found here can be explained by a VARX model with the addition of a divisive gain adaptation mechanism … The noise-quenching result and its explanation via gain adaptation shows the benefit of using a parsimonious linear model, which can suggest nonlinear mechanisms as simple corrections from linearity.”

Appraisal of whether the authors achieve their aims:

As a methodological advancement highlighting a limitation of existing approaches and presenting a new model to overcome it, the authors achieve their aim. Generally, the claims/conclusions are supported by the results.

The wider neuroscience claims regarding the role of intrinsic dynamics and external inputs in affecting brain data could benefit from further replication with another independent dataset and in a variety of tasks - but I understand if the authors wanted to focus on the method rather than the neuroscientific claims in this manuscript.

We fully agree. We added the following to the Discussion section:

“Future studies should test if our findings replicate in an independent iEEG datasets, including active tasks and whether they generalize to other neuroimaging modalities.”

Impact:

The authors propose a useful new approach that solves an important problem in the analysis of task neuroimaging data. I believe the work can have a significant impact on the field.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

Minor comments:

(1) Did you mean "less" or "fewer" in the following sentence "..larger values lead to overfitting, i.e. less significant connections..."?

We mean fewer. Thanks for catching this. 

(2) I didn't see any equations showing how the regularization parameter lambda is incorporated into the framework.

We prefer the math and details of the algorithm to an earlier paper that has now been published. Instead we added the following clarification: 

“The VARX models were fitted to data with the matlab version of the code31 using conventional L2-norm regularization. The corresponding regularization parameter was set to 𝜆=0.3.”

(3) I think some readers of this might struggle to understand the paragraph beginning

"Connectivity plots are created with nilearn's plot_connectome() function...". It's all quite opaque for the uninitiated.

Agreed. We now write more simply: 

“Connectivity plots in Fig. 4 were created with routines from the nilearn toolbox [51].”

(4) The paragraph beginning "The length of responses for Figure 5..." is also very opaque and could do with being explained more fully. Or this text could be removed from the methods and incorporated into the relevant results section where you actually discuss this analysis.

Thank you for flagging this. We expand on the details in the Methods as follows: 

“The length of responses for each channel in B and H to external inputs in Fig. 5 is computed with Matlab's findpeaks() function. This function returns the full-width at half of the peak maximum minus baseline. Power in each channel is computed as the squares of the responses averaged over the time window that was analyzed (0-0.6s).”

(5) I think adding some comments to the text or caption related to Figures 3C and 3D would be helpful so readers can understand these numbers a bit better. One seems to be the delta log p value and the other is the delta ratio. What does positive or negative mean? Readers might appreciate a little more help.

We expanded it as follows, hopefully this helps: 

“C) difference of log for VAX model without minus with inputs (panel A - B). Both models are fit to the same data. D) Thresholding panels A and B at p<0.0001 gives a fraction of significant connections. Here we show the fraction of significant channels for models with and without input. Each line is a patient with color indicating increase or decrease  E) Mean over all channels for VARX models with and without inputs. Each line is a patient.”

(6) It is not clear what the colors mean in Figures 4 E, F, G.

We updated the color scheme for those figure panels and carefully explained it in the caption. Please see the manuscript for updated figure 4.   

(7) It might be nice to slightly unpack what you mean by the "variability of the internal dynamic" and why it can be equated with the power of the innovation process.

In the methods we added the following clarification right after defining the VARX model: 

“The innovation process captures the internal variability of the model. Without it, repeating the same input would always result in a fixed deterministic output .”

In the results section we added the following: 

“As a metric of internal variability we measured the power of the intrinsic innovation process , which captures the unobserved “random” brain activity which leads to variations in the responses.”

(8) Typos etc.

a) "... has been attributed to variability of ongoing dynamic"

b) The manuscript refers to a Figure 3G, but there is no Figure 3G.

c) n_a = n_a = 1. Is that a typo?

d) fiction

Thank you for catching these. We fixed them. 

Reviewer #2 (Recommendations for the authors):

(1) I'm curious about the authors' opinions on the conditions studied. Naively, eyes open rest and passive movie watching seem like similar conditions - were the authors expecting to see a difference with VARX? Do the authors expect that they would see bigger differences when there is a larger difference in sensory input, e.g. eyes closed rest vs movie watching? Given the authors are arguing the need to explicitly model external inputs, a real data example contrasting two very different external inputs might better demonstrate the model's utility.

Thank you for this suggestion. We added an analysis of eyes-closed rest recordings, available in 8 patients (Fig. S8). The difference between movie and rest is indeed more pronounced than for eyes open rest. The result is described in the methods:

“In a subset of patients with eyes-closed resting state we find the same effect, that is qualitatively more pronounced (Fig. S8).”

This complements our updated finding of a difference between movie and eyes-open rest that does show a significant difference after adding more data to this analysis. The results have been updated as following

“The number of significant recurrent connections in  were significantly reduced during  movie watching compared to rest (Fig. 4C, fixed effect of stimulus:

beta = -3.8*10^-3, t(17) = -3.9, p<0.001), as is the effect size R (Fig. 4D, fixed effect of stimulus: beta = -2.5*10^-4, t(17) = -4.1, p<0.001).”

The abstract has been updated accordingly:

“We also find that the recurrent connectivity during rest is reduced during movie watching.”

(2) It would also have been interesting to see how the proposed model compares to DCM - however, I understand if the authors wanted to focus on their model rather than a comparison with other models.

We did not try the DCM for a number of reasons. 1) it does not allow for delays in the model dynamic (i.e. the entire time course of the response has to be captured by the recurrent dynamic of a single time step A). 2. It is computationally prohibitive and would not allow us to analyze large channel counts. 3. The available code is custom made for fMRI or EEG analysis with very specified signal generation models that do not obviously apply to iEEG. We added the following to the Discussion of the CDM:  

“Similar to the VARX model, DCM includes intrinsic and extrinsic effects A and B. However, the modeling is limited to first-order dynamics (i.e. η_a=η_b=1). Thus, prolonged responses have to be entirely captured with a first-order recurrent A. … In contrast, here we have analyzed up to 300 channels per subject across the brain, which would be prohibitive with DCM. By analyzing a large number of recordings we were able to draw more general conclusions about whole-brain activity.”

(3) I believe improving the consistency of the terminology used would improve the manuscript:

a) Intrinsic dynamics vs intrinsic connectivity vs recurrent connectivity:

- The term 'intrinsic dynamic' is first introduced in paragraph 3 of the introduction. An explicit definition of is meant by this term would benefit the manuscript.

- Sometimes the terminology changes to 'intrinsic connectivity' or 'recurrent connectivity'. An explicit definition of these terms (if they refer to different things) would also benefit the manuscript.

We had used the term “intrinsic” and “recurrent” interchangeably. We now try to mostly say “intrinsic dynamic” when we talk about the more general phenomenon or recurrent brain dynamic, while using “recurrent connectivity” when we refer to the model parameters A. 

We provide now a definition already at the start of the Abstract: 

“Sensory stimulation of the brain reverberates in its recurrent neural networks. However, current computational models of brain activity do not separate immediate sensory responses from this intrinsic dynamic. We apply a vector-autoregressive model with external input (VARX), combining the concepts of “functional connectivity” and “encoding models”, to intracranial recordings in humans. This model captures the extrinsic effect of the stimulus and separates that from the intrinsic effect of the recurrent brain dynamic.”

And at the start of the introduction: 

“The primate brain is highly interconnected between and within brain areas. … We will refer to the dynamic driven by this recurrent architecture as the intrinsic dynamic of the brain.”

b) Intrinsic vs Endogenous and Extrinsic vs Exogenous:

- Footnote 1 defines the 'intrinsic' and 'extrinsic' terminology.

- However, there are instances where the authors switch back to endogenous/exogenous.

- Methods section: "Overall system response", paragraph 2.

- Results section: "Recurrent dynamic enhances and prolongs stimulus responses".

- Conclusions section.

With a foot in both neuroscience and systems identification, it’s a hard habit to break. Thanks for catching it. We searched and replaced all instances of endogenous and exogenous.  

(4) Methods:

a) The model equation would be clearer if the convolution was written out fully. (I had to read reference 1 to understand the model.).

We now spell out the full equation and hope it's not too cumbersome to read:  

“For the th signal channel the recurrence of the VARX model is given by: 

”

b) How is an individual dimension omitted in the reduced model, are the values in the y, x set to zero?

No, it is actually removed from the linear prediction. We added: 

“… omitted from the prediction …”

c) "The p-value quantifies the probability that a specific connection in A or B is zero" - for each of n_a/n_b filters?

d) It should be clarified that D is a vector.

We hope the following clarification addresses both these questions: 

“The p-value quantifies the probability that a specific connection in either A or B is zero. Therefore, D,P and R² all have dimensions or for A or B  respectively.”

(5) Results:

a) Stimulus-induced reduction of noise in the intrinsic activity: would be good to define the frequency range for theta and beta in paragraph 2.

Added. 

b) Neural mass model simulation:

- A brief description of what was simulated is needed.

We basically ran the sample code of the neurolib library. With that in mind maybe the description we already provide is sufficient:  

“We used the default model simulation of the neurolib python library (using their sample code for the “ALNModel”), which is a mean-field approximation of adaptive exponential integrate-and-fire neurons. This model can generate simulated mean firing rates in 80 brain areas based on connectivity and delay matrices determined with diffusion tensor imaging (DTI). We used 5 min of “resting state” activity (no added stimulus, simulated at 0.1ms resolution, subsequently downsampled to 100Hz).”

- It's not clear to me why the A matrix should match the structural connectivity.

We added the following introduction to make the purpose of this simulation clear:

“To test the descriptive validity [43] of the VARX model we follow the approach of recovering structural connectivity from functional activity in simulation. [44] Specifically, we will compare the “connectivity” A derived from brain activity simulated assuming a given structural connectivity, i.e. we ask, can the VARX model recover the underlying structural connectivity, at least in a simulated whole-brian model with known connectivity?”

- It would be interesting to see the inferred A matrix.

We added a Supplement figure for this and the following: 

“The VARX model was estimated with n_a=2, and no input. The resulting estimate for A is dominated by the diagonal elements that capture the autocorrelation within brain areas (Fig. S1).”

- How many filters were used here?

No input filters were used for this simulation:

We used 5 min of “resting state” activity (no added stimulus, simulated at 0.1ms resolution, subsequently downsampled to 100Hz). 

c) Intracranial EEG:

- It's not clear how overfitting was measured and how the selection of the number of filters (n_a and n_b) was done.

We have removed the statement about overfitting. Mostly the word is used in the context of testing on a separate dataset, which we did not do here. So this “overfitting” can be confusing. Instead we used the analytic p-value as indication that a larger model order is not supported by the data. We write this now as follows: 

“Increasing the number of delays n_a, increases estimated effect size R (Fig. S3A,B), however, larger values lead to fewer significant connections (Fig. S3C). Significance (p-value) is computed analytically, i.e. non-parametrically, based on deviance. Values around n_a=6 time delays appear to be the largest model order supported by this statistical analysis.”

d) Figure 1:

- Typo: "auto-regressive"

Fixed. Thanks for catching that. 

- LFP and BHA in C are defined much later in the text, would be useful to define these in the caption. o Shouldn't B (the VARX model parameter) be a 2x3 matrix for different time lags?

Hopefully the following clarifications address both these points: 

“C) Example of neural signal y(t) recorded at a single location in the brain. We will analyze local field potentials (LFP) and broad-band high frequency activity (BHA) in separate analyses.  D) Examples of filters B for individual feed-forward connections between an extrinsic input and a specific recording location in the brain.”

(6) Discussion:

I could not find Muller et al 2016 listed in the references.

Added. Thanks for catching that omission. 

Additional edits prompted by reviewers, but not in the context of any particular comment.

While reviewers did not raise this following point, we felt the need clarify the terminology in the Methods to make sure there is not misunderstanding in the proposed interpretation of the model: 

“We will refer to the filters in matrix A and B and as recurrent and feed-forward “connections”, but avoid the use of the word “causal” which can be misleading.”

In addressing questions to Figure 4, we noticed that there is quite a bit of variability across patients, so the analysis for Figure 4 and 7 which combines data across patients now accounts for a random effect of patient (previously we have used mean values for repeated measures). We added the following to the Methods to explain this:

“To compare recurrent connectivity between movies and the resting-state (in Fig. 4), we compute VARX models in four different movie segments of 5 minutes length to match the length of the resting state recording. We use the first and second half of ‘Despicable Me English’, the first half of ‘Inscapes’ and one of the ‘Monkey’ movies. 18 patients include each of these recordings. For each recording in each patient we compute the fraction of significant channels (p<0.001) and average the effect size R across all channel pairs, excluding the diagonal. We test the difference between movies and resting-state with linear mixed-effect models with stimulus as fixed effect (movie vs rest), and patient as random effect (to account for the repeated measures for the different video segments), using matlab’s fitlme() routine. For the analysis of asymmetry of recurrent connectivity (in Fig. 4) we also used a mixed-effect model with T1w/T2w ratio as fixed effect and patients as random effect (to account for the repeated measures in multiple brain locations).”

All analyses were rerun with more data (eyes closed resting) and 2 additional patients that have become available since the first submission. Therefore all figures and statistics have been updated throughout the paper. Other than the difference between movies and resting state which was trending before and is now significant, no results changed.

Author response:

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

Reviewer 1:

Comment 0: In this paper, the authors develop a comprehensive program to investigate the organization of chromosome structures at 100 kb resolution. It is extremely well executed. The authors have thought through all aspects of the problem. The resulting software will be most useful to the community. Interestingly they capture many experimental observations accurately.

I have very few complaints.

We appreciate the reviewer’s strong assessment of the paper’s significance, novelty, and broad interest, and we thank them for the detailed suggestions and comments.

Comment 1: The number of parameters in the energy function is very large. Is there any justification for this? Could they simplify the functions?

We extend our gratitude to the reviewer for their insightful remarks. The parameters within our model can be categorized into two groups: those governing chromosome-chromosome interactions and those governing chromosome-nuclear landmark interactions.

In terms of chromosome-chromosome interactions, the parameter count is relatively modest compared to the vast amount of Hi-C data available. For instance, while the whole-genome Hi-C matrix at the 100KB resolution encompasses approximately 303212 contacts, our model comprises merely six parameters for interactions among different compartments, along with 1000 parameters for the ideal potential. As outlined in the supporting information, the ideal potential is contingent upon sequence separation, with 1000 chosen to encompass bead separations of up to 100MB. While it is theoretically plausible to reduce the number of parameters by assuming interactions cease beyond a certain sequence separation, determining this scale a priori presents a challenge.

During the parameterization process, we observed that interchromosomal contacts predicted solely based on compartmental interactions inadequately mirrored Hi-C data. Consequently, we introduced 231 additional parameters to more accurately capture interactions between distinct pairs of autosomes. These interactions may stem from factors such as non-coding RNA or proteins not explicable by simple, non-specific compartmental interactions.

Regarding parameters concerning chromosome-nuclear landmark interactions, we have 30321 parameters for speckles and 30321 for the nuclear lamina. To streamline the model, we opted to assign a unique parameter to each chromatin bead. However, it is conceivable that many chromatin beads share a similar mechanism for interacting with nuclear lamina or speckles, potentially allowing for a common parameter assignment. Nonetheless, implementing such simplification necessitates a deeper mechanistic understanding of chromosome-nuclear landmark interactions, an aspect currently lacking.

As our comprehension of nuclear organization progresses, the interpretability of parameter counts may improve, facilitating their reduction.

Comment 2: What would the modification be if the resolution is increased?

To increase the resolution of chromatin, we can in principle keep the same energy function as defined in Eq. S6. In this case, we only need to carry out further parameter optimization.

However, transitioning to higher resolutions may unveil additional features not readily apparent at 100kb. Notably, chromatin loops with an average size of 200kb or smaller have been identified in high-resolution Hi-C data [1]. To effectively capture these loops, new terms in the energy function must be incorporated. For instance, Qi and Zhang [2] employed additional contact potentials between CTCF sites to account for loop formation. Alternatively, an explicit loop-extrusion process could be introduced to model loop formation more accurately.

Comment 3: They should state that the extracted physical values are scale-dependent. For example, viscosity.

We thank the reviewer for the comment and would like to clarify that our model does not predict the viscosity. The nucleoplasmic viscosity was set as 1Pa · s to produce a diffusion coefficient that reproduces experimental value. The exact value for the nucleoplasmic viscosity is still rather controversial, and our selected value falls in the range of reported experimental values from 10−1Pa·s to 102Pa · s.

We have modified the main text to clarify the calculation of the diffusion coefficient.

“The exponent and the diffusion coefficient Dα = (27±11)×10−4μm2 · s−α both match well with the experimental values [cite], upon setting the nucleoplasmic viscosity as 1Pa · s (see Supporting Information Section: Mapping the reduced time unit to real time for more details).”

Reviewer 2:

Comment 0: In this work, Lao et al. develop an open-source software (OpenNucleome) for GPU-accelerated molecular dynamics simulation of the human nucleus accounting for chromatin, nucleoli, nuclear speckles, etc. Using this, the authors investigate the steady-state organization and dynamics of many of the nuclear components.

We thank the reviewer for summary of our work.

Comment 1: The authors could introduce a table having every parameter and the optimal parameter value used. This would greatly help the reader.

We would like to point out that model parameters are indeed provided in Table S1, S2, S3, S4, and Fig. S7. In these tables, we further provided details on how the parameters were determined.

Given the large number of parameters for the ideal potential (1000), we opted to plot it rather than listing out all the numbers. We added three new figures to plot the interaction parameters between chromosomes, between chromosomes and speckles, and between chromosomes and the nuclear lamina. Numerical values can be found online in the GitHub repository (parameters).

Comment 2: How many total beads are simulated? Do all beads have the same size?

The total number of the coarse-grained beads is 70542, including 60642 chromatin beads, 300 nucleolus beads, 1600 speckle beads, and 8000 nuclear lamina beads. The radius of the chromatin, nucleolus, and speckle beads is 0.25, while that of the lamina bead is 0.5. More information of the size and number of the beads are discussed in the Section: Components of the whole nucleus model.

Comment 3: In Equation S17, what is the 3rd and 4th powers mean? What necessitates it?

The potential defined in Equation S17 follows the definition of class2 bond in the LAMMPS package (LAMMPS docs). Compared to a typical harmonic potential, the presence of higher order terms produces sharper increase in the energy at large distances (Author response image 1). This essentially reduces the flucatuation of bond length in simulations.

Author response image 1.

Comparison between the Class2 potential (defined in Eq. S17) and the Harmonic potential (K(r − r0)2, with K = 20 and r0 = 0.5).

Comment 4: What do the X-axis and Y-axis numbers in Figure 5A and 5B mean? What are their units?

We apologize for the lack of clarify in our original figure. In Fig. 5A, the X and Y axis depicts the simulated and experimental radius of gyration (Rg) for individual chromosomes, as indicated in the title of the figure. Similarly, in Fig. 5B, the X and Y axis depicts the simulated and experimental radial position of individual chromosomes.

We have converted the chromosome Rg values into reduced units and labeled the corresponding axes in the updated figure (Fig. 5). The normalized radial position is unitless and its detailed definition is included in the supporting information Section: Computing simulated normalized chromosome radial positions. We updated the figure caption to provide an explicit reference to the SI text.

Reviewer 3:

Comment 0: In this work, the authors present the development of OpenNucleome, a software for simulating the structure and dynamics of the human nucleus. It provides a detailed model of nuclear components such as chromosomes and nuclear bodies, and uses GPU acceleration for better performance based on the OpenMM package. The work also shows the model’s accuracy in comparisons with experimental data and highlights the utility in the understanding of nuclear organization. While I consider this work a good tool for the genome architecture scientific community, I have some comments and questions that could further clarify the usage of this tool and help potential users. I also have a few questions that would help to clarify the technique and results and some suggestions for references.

We appreciate the reviewer’s strong assessment of the paper’s significance, novelty, and broad interest, and we thank them for the detailed suggestions and comments.

Comment 1: Could the authors elaborate on what they consider to be ’well-established and easily adoptable modeling tools’?

By well established, we meant that models that have been extensively validated and verified, and are highly regarded by the community.

By easily adoptable, we meant that tools that are well documented and can be relatively easily learned by new groups without help from the developers.

We have revised the text to clarify our meaning.

“Despite the progress made in computational modeling, the absence of well-documented software with easy-to-follow tutorials pose a challenge.”

Comment 2: Recognizing the value of a diverse range of tools in the community, the Open-MiChroM tool is also an open-source platform built on top of OpenMM. The documentation shows various modeling approaches and many tutorials that contain different approaches besides the MiChroM energy function. How does OpenNucleome compare in terms of facilitating crossvalidation and user accessibility? The two tools seem to be complementary, which is a gain to the field. I recommend adding one or two sentences in the matter. Also, while navigating the OpenNucleome GitHub, I have not found the tutorials mentioned in the text. I also consider a barrier in the process of generating necessary input files. I would suggest expanding the tutorials and documentation to help potential users.

We thank the reviewer for the excellent comments. We agree that while many of the tutorials were included in the original package, they were not as clearly documented. We have revised them extensively to to now present:

• A tutorial for optimizing chromosome chromosome interactions.

• A tutorial for optimizing chromosome nuclear landmark interactions.

• A tutorial for building initial configurations.

• A tutorial for relaxing the initial configurations.

• A tutorial for selecting the initial configurations.

• A tutorial for setting up performing Langevin dynamics simulations.

• A tutorial for setting up performing Brownian dynamics simulations.

• A tutorial for setting up performing simulations with deformed nucleus.

• A tutorial for analyzing simulation trajectories.

• A tutorial for introducing new features to the model.

These tutorials and our well-documented and open source code (https://zhanggroup-mitchemistry.github.io/OpenNucleome) should significantly promote user accessibility. Our inclusion of python scripts for analyzing simulation trajectorials shall allow users to compute various quantities for evaluating and comparing model quality.

We added a new paragraph in the Section: Conclusions and Dicussion of the main text to compare OpenNucleosome with existing software for genome modeling.

“Our software enhances the capabilities of existing genome simulation tools [cite]. Specifically, OpenNucleome aligns with the design principles of Open-MiChroM [cite], prioritizing open-source accessibility while expanding simulation capabilities to the entire nucleus. Similar to software from the Alber lab [cite], OpenNucleome offers highresolution genome organization that faithfully reproduces a diverse range of experimental data. Furthermore, beyond static structures, OpenNucleome facilitates dynamic simulations with explicit representations of various nuclear condensates, akin to the model developed by [citet].”

Comment 3: Lastly, I would appreciate it if the authors could expand their definition of ’standardized practices’.

We apologize for any confusion caused. By ”standardized practices,” we refer to the fact that different groups often employ unique procedures for structural modeling. These procedures differ in the representation of chromosomes, the nucleus environment, and the algorithms for parameter optimization. This absence of a consensus on the optimal practices for genome modeling can be daunting for newcomers to the field.

We have revised the text to the following to avoid confusion:

“Many research groups develop their own independent software, which complicates crossvalidation and hinders the establishment of best practices for genome modeling [3–5].”

Comment 4: On page 7, the authors refer to the SI Section: Components of the whole nucleus model for further details. Could the authors provide more information on the simulated density of nuclear bodies? Is there experimental data available that details the ratio of chromatin to other nuclear components, which was used as a reference in the simulation?

We thank the reviewer for the comment. Imaging studies have provided quantitative measures about the size and number of various nuclear bodies. For example, there are 2 ∼ 5 nucleoli per nucleus, with the typical size RNo ≈ 0.5μm [6–10]. In the review by Spector and Lamond [11], the authors showed that there are 20 ∼ 50 speckles, with the typical size RSp ≈ 0.3μm. We used these numbers to guide our simulation of nuclear bodies. These information was mentioned in the Section: Chromosomes as beads on the string polymers of the supporting information.

The chromatin density is fixed by the average size of chromatin bead and the nucleus size. We chose the size of chromatin based on imaging studies as detailed in the Subsection: Mapping chromatin bead size to real unit of the supporting information. Upon fixing the bead size, the chromatin volume is determined.

Comment 5: In the statement, ’the ideal potential is only applied for beads from the same chromosome to approximate the effect of loop extrusion by Cohesin molecules for chromosome compaction and territory formation,’ it would be helpful if the authors could clarify the scope of this potential. Specifically, the code indicates that the variable ’dend ideal’ is set at 1000, suggesting an interaction along a 100Mb polymer chain at a resolution of 100Kb per bead. Could the authors elaborate on their motivation for the Cohesin complex’s activity having a significant effect over such long distances within the polymer chain?

We thank the reviewer for the insight comment. They are correct that the ideal potential was introduced to capture chromosome folding beyond the interactions between compartments, including loop extrusion. Practically, we parameterized the ideal potential such that the simulated average contact probabilities as a function of sequence separation match the experimental values. The reviewer is correct that beyond a specific value of sequence separation, one would expect the impact of loop extrusion on chromosome folding should be negligible, due to Cohesin dissociation. Correspondingly, the interaction potential should be zero at large sequence separations.

However, it is important to note that the precise separation scale cannot be known a priori. We chose 100Mb as a conservative estimation. However, as we can see from Fig. S7, our parameterization scheme indeed produced interaction parameters are mainly zero at large sequence separations. Interesting, the scale at which the potential approaches 0 (∼ 500KB), indeed agree with the estimated length traveled by Cohesin molecules before dissociation [12].

Comment 6: On pages 8 and 9, the authors discuss the optimization process. However, in reviewing the code and documentation available on the GitHub page, I could not find specific sections related to the optimization procedure described in the paper. In this context, I have a few questions: Could the authors provide more details or direct me to the parts of the documentation and the text/SI that address the optimization procedure used in their study? Additional clarification on the cost/objective function employed during the optimization process would be highly beneficial, as this was not readily apparent in the text.

We thank the reviewer for the comment. We revised the SI to include the definition of the cost function for the Adam optimizer.

“During the optimization process, our aim was to minimize the disparity between experimental findings and simulated data. To achieve this, we defined the cost function as follows:

where the index i iterates over all the constraints defined in Eq. S28.”

The detailed optimization procedure was included in the SI as quoted below

“The details of the algorithm for parameter optimization are as follows

(1) Starting with a set of values for and we performed 50 independent 3-million-step long MD simulations to obtain an ensemble of nuclear configurations. The 500K steps of each trajectory are discarded

as equilibration. We collected the configurations at every 2000 simulation steps from the rest of the simulation trajectories to compute the ensemble averages defined on the left-hand side of Eq. S13.

(2) Check the convergence of the optimization by calculating the percentage of error

defined as . The summation over i includes all the average contact probabilities defined in Eq. S28.

(3) If the error is less than a tolerance value etol, the optimization has converged, and we stop the simulations. Otherwise, we update the parameters, α, using the Adam optimizer [13]. With the new parameter values, we return to step one and restart the iteration.”

Previously, the optimization code was included as part of the analysis folder. To avoid confusion and improve readability, a separate folder named optimization has been created. This folder provides the Adam optimization of chromosome-chromosome interactions (chr-chr optimization) and chromosome-nuclear landmarks interactions (chr-NL optimization).

Comment 7: What was the motivation for choosing the Adam algorithm for optimization? Adam is designed for training on stochastic objective functions. Could the authors elucidate on the ’stochastic’ aspect of their function to be optimized? Why the Adam algorithm was considered the most appropriate choice for this application?

We thank the reviewer for the comment. As defined in Eq. R1, the cost function measures the difference between the simulated constraints with corresponding experimental values. The estimation of simulation values, by averaging over an ensemble of chromosome configurations, is inherently noisy and stochastic. Exact ensemble averages can only be achieved with unlimited samples obtained from infinite long simulations.

In the past, we have used the Newton’s method for parameterization, and the detailed algorithm can be found in the SI of Ref. 14. However, we found that Adam is more efficient as it is a first-order approximation method. The Newton’s method, on the other hand, is second-order approximation method and requires estimation of the Hessian matrix. When the number of constraints is large, as is in our case, the computational cost for estimating the Hessian matrix can be significant. Another advantage of the Adam algorithm lies in its adjustment of the learning rate along the optimization to further speedup convergence.

Comment 8: The authors mention that examples of setting up simulations, parameter optimization, and introducing new features are provided in the GitHub repository. However, I was unable to locate these examples. Could the authors guide me to these specific resources or consider adding them if they are not currently available?

We thank the reviewer for the comment. We have improved the GitHub repository and all the tutorials can be found using the links provided in Response to Comment 2.

Comment 9: Furthermore, the paper states that ’a configuration file that provides the position of individual particles in the PDB file format is needed to initialize the simulations.’ It would be beneficial for new users if the authors could elaborate on how this file is generated. And all other input files in general. Detailing the procedures for a new user to run their system using OpenNucleome would be helpful.

We thank the reviewer for the comment. The procedure for generating initial configurations was explained in the SI Section: Initial configurations for simulations and quoted below.

“We first created a total of 1000 configurations for the genome by sequentially generating the conformation of each one of the 46 chromosomes as follows. For a given chromosome, we start by placing the first bead at the center (origin) of the nucleus. The positions of the following beads, i, were determined from the (i − 1)-th bead as . v is a normalized random vector, and 0.5 was selected as the bond length between neighboring beads. To produce globular chromosome conformations, we rejected vectors, v, that led to bead positions with distance from the center larger than 4σ. Upon creating the conformation of a chromosome i, we shift its center of mass to a value ri com determined as follows. We first compute a mean radial distance, with the following equation

where Di is the average value of Lamin B DamID profile for chromosome i. Dhi and Dlo represent the highest and lowest average DamID values of all chromosomes, and 6σ and 2σ represent the upper and lower bound in radial positions for chromosomes. As shown in Fig. S6, the average Lamin B DamID profiles are highly correlated with normalized chromosome radial positions as reported by DNA MERFISH [cite], supporting their use as a proxy for estimating normalized chromosome radial positions. We then select as a uniformly distributed random variable within the range . Without loss of generality, we randomly chose the directions for shifting all 46 chromosomes.

We further relaxed the 1000 configurations to build more realistic genome structures. Following an energy minimization process, one-million-step molecular dynamics (MD) simulations were performed starting from each configuration. Simulations were performed with the following energy function

where UGenome is defined as in Eq. S7. UG-La is the excluded volume potential between chromosomes and lamina, i.e, only the second term in Eq. S24. Parameters in UGenome were from a preliminary optimization. The end configurations of the MD simulations were collected to build the final configuration ensemble (FCE).”

The tutorial for preparing initial configurations can be found at this link.

Comment 10: In the section discussing the correlation between simulated and experimental contact maps, as referenced in Figure 4A and Figure S2, the authors mention a high degree of correlation. Could the authors specify the exact value of this correlation and explain the method used for its computation? Considering that comparing two Hi-C matrices involves a large number of data points, it would be helpful to know if all data points were included in this analysis.

We have updated Fig 4A and S2 to include Pearson correlation coefficients next to the contact maps. The reviewer is correct in that all the non-redundant data points of the contact maps are included in computing the correlation coefficients.

For improved clarity, we added a new section in the supporting information to detail the calculations. The section is titled Computing Pearson correlation coefficients between experimental and simulated contact maps, and the relevant text is quoted below.

“We computed the Pearson correlation coefficients (PCC) between experimental and simulated contact maps in Fig. 4A and Fig. S2 as

xi and yi represent the experimental and simulated contact probabilities, and n is the total number of data points. Only non-redundant data points, i.e., half of the pairwise contacts, are used in the PCC calculation.”

Comment 11: In addition, the author said: ”Moreover, the simulated and experimental average contact probabilities between pairs of chromosomes agree well, and the Pearson correlation coefficient between the two datasets reaches 0.89.” How does this correlation behave when not accounting for polymer compaction or scaling? An analysis presenting the correlation as a function of genomic distance would be interesting.

Author response image 2.

Pearson correlation coefficient between experimental and simulated contact probabilities as a function of the sequence separation within specific chromosomes. For each chromosome, we first gathered a set of experimental contacts alongside a matching set of simulated ones for genomic pairs within a particular separation range. The Pearson correlation coefficient at the corresponding sequence separation was then determined using Equation R4. We limited the calculations to half of the chromosome length to ensure the availability of sufficient data.

We thank the reviewer for the comment. The analysis presenting the correlation as a function of genomic distance (sequence separation) for each chromosome is shown in Figure S12 and also included in the SI. While the correlation coefficients decreases at larger separation, the values around 0.5 is quite reasonable and comparable to results obtained using Open-Michrom.

We also computed the correlation of whole genome contact maps after excluding intra-chromosomal contacts. The PCC decreased from 0.89 to 0.4. Again, the correlation coefficient is quite reasonable considering that these contacts are purely predicted by the compartmental interactions and were not directly optimized.

Comment 12: I recommend using the web-server that is familiar to the authors to benchmark the OpenNucleome tool/model: ”3DGenBench: A Web-Server to Benchmark Computational Models for 3D Genomics.” Nucleic Acids Research, vol. 50, no. W1, July 2022, pp. W4-12.

We appreciate the reviewer’s suggestion. Unfortunately, the website is no longer active during the time of the revision. However, as detailed in Response to comment 11, we used the one of the popular metrics to exclude polymer compact effect and evaluate the agreement between simulation and experiments.

Comment 13: Regarding the comparison of simulation results with microscopy data from reference 34. Given their different resolutions and data point/space groupings, how do the authors align these datasets? Could the authors describe how they performed this comparison? How were the radial positions calculated in both the simulations and experiments? Since the data from reference 34 indicates a non-globular shape of the nucleus; how did this factor into the calculation of radial distributions?

We thank the reviewer for the comment and apologize for the confusion. First, the average properties we examined, including radial positions and interchromosomal contacts, were averaged over all genomic loci. Therefore, they are independent of data resolution.

Secondly, instead of calculating the absolute radial positions, which are subject to variations in nucleus shape and size, we defined the normalized radial positions. They measure the ratio between the distance from the nucleus center to the chromosome center and the distance from the nucleus center to the lamina. This definition was frequently used in prior imaging studies to measure chromosome radial positions.

The calculation of the simulated normalized radial positions and the experimental normalized radial positions are discussed in the Section: Computing simulated normalized chromosome radial positions

“For a given chromosome i, we first determined its center of mass position denoted as Ci. Starting from the center of the nucleus, O, we extend the the vector vOC to identify the intersection point with the nuclear lamina as Pi. The normalized chromosome radial position i is then defined as , where ||·|| represents the L2 norm.

and Section: Computing experimental normalized chromosome radial positions.

“We followed the same procedure outlined in Section: Computing simulated normalized chromosome radial positions to compute the experimental values. To determine the center of the nucleus using DNA MERFISH data, we used the algorithm, minimum volume enclosing ellipsoid (MVEE)[15], to fit an ellipsoid for each genome structure. The optimal ellipsoid defined as is obtained by optimizing subjecting to the constraint that . xi correspond to the list of chromatin positions determined experimentally.”

Comment 14: In the sentence: ”It is evident that telomeres exhibit anomalous subdiffusive motion.” I recommend mentioning the work ”Di Pierro, Michele, et al., ”Anomalous Diffusion, Spatial Coherence, and Viscoelasticity from the Energy Landscape of Human Chromosomes.” Proceedings of the National Academy of Sciences, vol. 115, no. 30, July 2018, pp. 7753-58.”.

We have revised the sentence to include the citation as follows.

“In line with previous research [cite], telomeres display anomalous subdiffusive motion. When fitted with the equation , these trajectories yield a spectrum of α values, with a peak around 0.59.”

Comment 15: Regarding the observation that ’chromosomes appear arrested and no significant changes in their radial positions are observed over timescales comparable to the cell cycle,’ could the authors provide more details on the calculations or analyses that led to this conclusion? Specifically, information on the equilibration/relaxation time of chromosome territories relative to rearrangements within a cell cycle would be interesting.

Our conclusion here was mostly based on the time trace of normalized radial positions shown in Figure 6A of the main text. Over the timescale of an entire cell cycle (24 hours), the relatively little to no changes in the radial positions supports glassy dynamics of chromosomes. We further determined the mean squared displacement (MSD) for chromosome center of masses. As shown in the left panel of Fig. S12, the MSDs are much smaller than the average size of chromosomes (see Rg values in Fig. 5A), supporting arrested dynamics.

We further computed the auto-correlation function of the normalized chromosome radial position as

where t indexes over the trajectory frames and ¯r is the mean position. As shown in Fig. S12, the positions are not completely decorrelated over 10 hours, again supporting slow dynamics. It would be interesting to examine the relaxation timescale more closely in future studies.

Comment 16: The authors also comment on the SI ”Section: Initial configurations for simulations provides more details on preparing the 1000 initial configurations.” and related to reference 34 mentioning that ”the average Lamin B DamID profiles are highly correlated with chromosome radial positions as reported by DNA MERFISH”. How do the authors account for situations where homologous chromosomes are neighbors or have an interacting interface? Ref. 34 indicates that distinguishing between these scenarios can be challenging, potentially leading to ’invalid distributions’ that are filtered out. Clarification on how such cases were handled in the simulations would be helpful.

We would like to first clarify that when comparing with experimental data, we averaged over the homologous chromosomes to obtain haploid data. We added the following text in the manuscript to emphasize this point

“Given that the majority of experimental data were analyzed for the haploid genome, we adopted a similar approach by averaging over paternal and maternal chromosomes to facilitate direct comparison. More details on data analysis can be found in the Supporting Information Section: Details of simulation data analysis.”

Furthermore, we used the processed DNA MERFISH data from the Zhuang lab, which unambiguously assigns a chromosome ID to each data point. Therefore, the issue mentioned by the reviewer is not present in the procssed data. In our simulations, since we keep track of the explicit connection between genomic segments, the trace of individual chromosomes can be determined for any configuration. Therefore, there is no ambiguity in terms of simulation data.

Comment 17: When discussing the interaction with nuclear lamina and nuclear envelop deformation, I suggest mentioning the following studies: The already cited ref 52 and ”Contessoto, Vin´ıcius G., et al. ”Interphase Chromosomes of the Aedes Aegypti Mosquito Are Liquid Crystalline and Can Sense Mechanical Cues.” Nature Communications, vol. 14, no. 1, Jan. 2023, p. 326.”

We updated the text to include the suggested reference.

“Numerous studies have highlighted the remarkable influence of nuclear shape on the positioning of chromosomes and the regulation of gene expression [16, 17].”

Comment 18: The authors state that ’Tutorials in the format of Python Scripts with extensive documentation are provided to facilitate the adoption of the model by the community.’ However, as I mentioned, the documentation appears to be limited, and the available tutorials could benefit from further expansion. I suggest that the authors consider enhancing these resources to better assist users in adopting and understanding the model.

As detailed in the Response to Comment 2, we have updated the GitHub repository to better document the included Jupyter notebooks and tutorials.

Comment 19: In the Methods section, the authors discuss using Langevin dynamics for certain simulations and Brownian dynamics for others. Could the authors provide more detailed reasoning behind the choice of these different dynamics for different aspects of the simulation? Furthermore, it would be insightful to know how the results might vary if only one of these dynamics was utilized throughout the study. Such clarification would help in understanding the implications of these methodological choices on the outcomes of the simulations.

We thank the reviewer for the comment. As detailed in the supporting information Section: Mapping the Reduced Time Unit to Real Time, the Brownian dynamics simulations provide a rigorous mapping to the biological timescale. By choosing a specific value for the nucleoplasmic viscosity, we determined the time unit in simulations as τ = 0.65s. With this time conversion, the simulated diffusion coefficients of telomeres match well with experimental values. Therefore, Brownian dynamics simulations are recommended for computing time dependent quantities and the large damping coefficients mimics the complex nuclear environment well.

On the other hand, the large damping coefficient slows down the configuration relaxation of the system significantly. For computing equilibrium statistical properties, it is useful to use a small coefficient and the Langevin integrator with large time steps to facilitate conformational relaxation.

References

[1] Rao, S. S.; Huntley, M. H.; Durand, N. C.; Stamenova, E. K.; Bochkov, I. D.; Robinson, J. T.; Sanborn, A. L.; Machol, I.; Omer, A. D.; Lander, E. S.; others A 3D map of the human genome at kilobase resolution reveals principles of chromatin looping. Cell 2014, 159, 1665–1680.

[2] Qi, Y.; Zhang, B. Predicting three-dimensional genome organization with chromatin states. PLoS computational biology 2019, 15, e1007024.

[3] Yildirim, A.; Hua, N.; Boninsegna, L.; Zhan, Y.; Polles, G.; Gong, K.; Hao, S.; Li, W.; Zhou, X. J.; Alber, F. Evaluating the role of the nuclear microenvironment in gene function by population-based modeling. Nature Structural & Molecular Biology 2023, 1–14.

[4] Junior, A. B. O.; Contessoto, V. G.; Mello, M. F.; Onuchic, J. N. A scalable computational approach for simulating complexes of multiple chromosomes. Journal of molecular biology 2021, 433, 166700.

[5] Fujishiro, S.; Sasai, M. Generation of dynamic three-dimensional genome structure through phase separation of chromatin. Proceedings of the National Academy of Sciences 2022, 119, e2109838119.

[6] Caragine, C. M.; Haley, S. C.; Zidovska, A. Nucleolar dynamics and interactions with nucleoplasm in living cells. Elife 2019, 8, e47533.

[7] Brangwynne, C. P.; Mitchison, T. J.; Hyman, A. A. Active liquid-like behavior of nucleoli determines their size and shape in Xenopus laevis oocytes. Proceedings of the National Academy of Sciences 2011, 108, 4334–4339.

[8] Farley, K. I.; Surovtseva, Y.; Merkel, J.; Baserga, S. J. Determinants of mammalian nucleolar architecture. Chromosoma 2015, 124, 323–331.

[9] Qi, Y.; Zhang, B. Chromatin network retards nucleoli coalescence. Nature Communications 2021, 12, 6824.

[10] Caragine, C. M.; Haley, S. C.; Zidovska, A. Surface fluctuations and coalescence of nucleolar droplets in the human cell nucleus. Physical review letters 2018, 121, 148101.

[11] Spector, D. L.; Lamond, A. I. Nuclear speckles. Cold Spring Harbor perspectives in biology 2011, 3, a000646.

[12] Banigan, E. J.; Mirny, L. A. Loop extrusion: theory meets single-molecule experiments. Current opinion in cell biology 2020, 64, 124–138.

[13] Kingma, D. P.; Ba, J. Adam: A method for stochastic optimization. arXiv preprint arXiv:1412.6980 2014,

[14] Zhang, B.; Wolynes, P. G. Topology, structures, and energy landscapes of human chromosomes. Proceedings of the National Academy of Sciences 2015, 112, 6062–6067.

[15] Moshtagh, N.; others Minimum volume enclosing ellipsoid. Convex optimization 2005, 111, 1–9.

[16] Brahmachari, S.; Contessoto, V. G.; Di Pierro, M.; Onuchic, J. N. Shaping the genome via lengthwise compaction, phase separation, and lamina adhesion. Nucleic Acids Res. 2022, 50, 1–14.

[17] Contessoto, V. G.; Dudchenko, O.; Aiden, E. L.; Wolynes, P. G.; Onuchic, J. N.; Di Pierro, M. Interphase chromosomes of the Aedes aegypti mosquito are liquid crystalline and can sense mechanical cues. Nature Communications 2023, 14, 326.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Mackie and colleagues compare chemosensory preferences between C. elegans and P. pacificus, and the cellular and molecular mechanisms underlying them. The nematodes have overlapping and distinct preferences for different salts. Although P. pacificus lacks the lsy-6 miRNA important for establishing asymmetry of the left/right ASE salt-sensing neurons in C. elegans, the authors find that P. pacificus ASE homologs achieve molecular (receptor expression) and functional (calcium response) asymmetry by alternative means. This work contributes an important comparison of how these two nematodes sense salts and highlights that evolution can find different ways to establish asymmetry in small nervous systems to optimize the processing of chemosensory cues in the environment.

Strengths:

The authors use clear and established methods to record the response of neurons to chemosensory cues. They were able to show clearly that ASEL/R are functionally asymmetric in P. pacificus, and combined with genetic perturbation establish a role for che-1-dependent gcy-22.3 in in the asymmetric response to NH₄Cl.

Weaknesses:

The mechanism of lsy-6-independent establishment of ASEL/R asymmetry in P. pacificus remains uncharacterized.

We thank the reviewer for recognizing the novel contributions of our work in revealing the existence of alternative pathways for establishing neuronal lateral asymmetry without the lsy-6 miRNA in a divergent nematode species. We are certainly encouraged now to search for genetic factors that alter the exclusive asymmetric expression of gcy-22.3.

Reviewer #2 (Public review):

Summary:

In this manuscript, Mackie et al. investigate gustatory behavior and the neural basis of gustation in the predatory nematode Pristionchus pacificus. First, they show that the behavioral preferences of P. pacificus for gustatory cues differ from those reported for C. elegans. Next, they investigate the molecular mechanisms of salt sensing in P. pacificus. They show that although the C. elegans transcription factor gene che-1 is expressed specifically in the ASE neurons, the P. pacificus che-1 gene is expressed in the Ppa-ASE and Ppa-AFD neurons. Moreover, che-1 plays a less critical role in salt chemotaxis in P. pacificus than C. elegans. Chemogenetic silencing of Ppa-ASE and Ppa-AFD neurons results in more severe chemotaxis defects. The authors then use calcium imaging to show that both Ppa-ASE and Ppa-AFD neurons respond to salt stimuli. Calcium imaging experiments also reveal that the left and right Ppa-ASE neurons respond differently to salts, despite the fact that P. pacificus lacks lsy-6, a microRNA that is important for ASE left/right asymmetry in C. elegans. Finally, the authors show that the receptor guanylate cyclase gene Ppa-gcy-23.3 is expressed in the right Ppa-ASE neuron (Ppa-ASER) but not the left Ppa-ASE neuron (Ppa-ASEL) and is required for some of the gustatory responses of Ppa-ASER, further confirming that the Ppa-ASE neurons are asymmetric and suggesting that Ppa-GCY-23.3 is a gustatory receptor. Overall, this work provides insight into the evolution of gustation across nematode species. It illustrates how sensory neuron response properties and molecular mechanisms of cell fate determination can evolve to mediate species-specific behaviors. However, the paper would be greatly strengthened by a direct comparison of calcium responses to gustatory cues in C. elegans and P. pacificus, since the comparison currently relies entirely on published data for C. elegans, where the imaging parameters likely differ. In addition, the conclusions regarding Ppa-AFD neuron function would benefit from additional confirmation of AFD neuron identity. Finally, how prior salt exposure influences gustatory behavior and neural activity in P. pacificus is not discussed.

Strengths:

(1) This study provides exciting new insights into how gustatory behaviors and mechanisms differ in nematode species with different lifestyles and ecological niches. The results from salt chemotaxis experiments suggest that P. pacificus shows distinct gustatory preferences from C. elegans. Calcium imaging from Ppa-ASE neurons suggests that the response properties of the ASE neurons differ between the two species. In addition, an analysis of the expression and function of the transcription factor Ppa-che-1 reveals that mechanisms of ASE cell fate determination differ in C. elegans and P. pacificus, although the ASE neurons play a critical role in salt sensing in both species. Thus, the authors identify several differences in gustatory system development and function across nematode species.

(2) This is the first calcium imaging study of P. pacificus, and it offers some of the first insights into the evolution of gustatory neuron function across nematode species.

(3) This study addresses the mechanisms that lead to left/right asymmetry in nematodes. It reveals that the ASER and ASEL neurons differ in their response properties, but this asymmetry is achieved by molecular mechanisms that are at least partly distinct from those that operate in C. elegans. Notably, ASEL/R asymmetry in P. pacificus is achieved despite the lack of a P. pacificus lsy-6 homolog.

Weaknesses:

(1) The authors observe only weak attraction of C. elegans to NaCl. These results raise the question of whether the weak attraction observed is the result of the prior salt environment experienced by the worms. More generally, this study does not address how prior exposure to gustatory cues shapes gustatory responses in P. pacificus. Is salt sensing in P. pacificus subject to the same type of experience-dependent modulation as salt sensing in C. elegans?

We tested if starving animals in the presence of a certain salt will result in those animals avoiding it. However, under our experimental conditions we were unable to detect experiencedependent modulation either in P. pacificus or in C. elegans.

Author response image 1.

(2) A key finding of this paper is that the Ppa-CHE-1 transcription factor is expressed in the PpaAFD neurons as well as the Ppa-ASE neurons, despite the fact that Ce-CHE-1 is expressed specifically in Ce-ASE. However, additional verification of Ppa-AFD neuron identity is required. Based on the image shown in the manuscript, it is difficult to unequivocally identify the second pair of CHE-1-positive head neurons as the Ppa-AFD neurons. Ppa-AFD neuron identity could be verified by confocal imaging of the CHE-1-positive neurons, co-expression of Ppa-che1p::GFP with a likely AFD reporter, thermotaxis assays with Ppa-che-1 mutants, and/or calcium imaging from the putative Ppa-AFD neurons.

In the revised manuscript, we provide additional and, we believe, conclusive evidence for our correct identification of Ppa-AFD neuron being another CHE-1 expressing neuron. Specifically, we have constructed and characterized 2 independent reporter strains of Ppa-ttx-1, a putative homolog of the AFD terminal selector in C. elegans. There are two pairs of ttx-1p::rfp expressing amphid neurons. The anterior neuronal pair have finger-like endings that are unique for AFD neurons compared to the dendritic endings of the 11 other amphid neuron pairs (no neuron type has a wing morphology in P. pacificus). Their cell bodies are detected in the newly tagged TTX-1::ALFA strain that co-localize with the anterior pair of che-1::gfp-expressing amphid neurons (n=15, J2-Adult).

We note that the identity of the posterior pair of amphid neurons differs between the ttx-1p::rfp promoter fusion reporter and TTX-1::ALFA strains– the ttx-1p::rfp posterior amphid pair overlaps with the gcy-22.3p::gfp reporter (ASER) but the TTX-1::ALFA posterior amphid pair do not overlap with the posterior pair of che-1::gfp-expressing amphid neurons (n=15). Given that there are 4 splice forms detected by RNAseq (Transcriptome Assembly Trinity, 2016; www.pristionchus.org), this discrepancy between the Ppa-ttx-1 promoter fusion reporter and the endogenous expression of the Ppa-TTX-1 C-terminally tagged to the only splice form containing Exon 18 (ppa_stranded_DN30925_c0_g1_i5, the most 3’ exon) may be due to differential expression of different splice variants in AFD, ASE, and another unidentified amphid neuron types.  

Although we also made reporter strains of two putative AFD markers, Ppa-gcy-8.1 (PPA24212)p::gfp; csuEx101 and Ppa-gcy-8.2 (PPA41407)p::gfp; csuEx100, neither reporter showed neuronal expression.

(3) Loss of Ppa-che-1 causes a less severe phenotype than loss of Ce-che-1. However, the loss of Ppa-che-1::RFP expression in ASE but not AFD raises the question of whether there might be additional start sites in the Ppa-che-1 gene downstream of the mutation sites. It would be helpful to know whether there are multiple isoforms of Ppa-che-1, and if so, whether the exon with the introduced frameshift is present in all isoforms and results in complete loss of Ppa-CHE-1 protein.

According to www.pristionchus.org (Transcriptome Assembly Trinity), there is only a single detectable splice form by RNAseq. Once we have a Ppa-AFD-specific marker, we would be able to determine how much of the AFD terminal effector identify (e.g. expression of gcy-8 paralogs) is effected by the loss of Ppa-che-1 function.

(4) The authors show that silencing Ppa-ASE has a dramatic effect on salt chemotaxis behavior. However, these data lack control with histamine-treated wild-type animals, with the result that the phenotype of Ppa-ASE-silenced animals could result from exposure to histamine dihydrochloride. This is an especially important control in the context of salt sensing, where histamine dihydrochloride could alter behavioral responses to other salts.

We have inadvertently left out this important control. Because the HisCl1 transgene is on a randomly segregating transgene array, we have scored worms with and without the transgene expressing the co-injection marker (Ppa-egl-20p::rfp, a marker in the tail) to show that the presence of the transgene is necessary for the histamine-dependent knockdown of NH₄Br attraction. This control is added as Figure S2.

(5) The calcium imaging data in the paper suggest that the Ppa-ASE and Ce-ASE neurons respond differently to salt solutions. However, to make this point, a direct comparison of calcium responses in C. elegans and P. pacificus using the same calcium indicator is required. By relying on previously published C. elegans data, it is difficult to know how differences in growth conditions or imaging conditions affect ASE responses. In addition, the paper would be strengthened by additional quantitative analysis of the calcium imaging data. For example, the paper states that 25 mM NH₄Cl evokes a greater response in ASEL than 250 mM NH₄Cl, but a quantitative comparison of the maximum responses to the two stimuli is not shown.

We understand that side-by-side comparisons with C. elegans using the same calcium indicator would lend more credence to the differences we observed in P. pacificus versus published findings in C. elegans from the past decades, but are not currently in a position to conduct these experiments in parallel.

(6) It would be helpful to examine, or at least discuss, the other P. pacificus paralogs of Ce-gcy22. Are they expressed in Ppa-ASER? How similar are the different paralogs? Additional discussion of the Ppa-gcy-22 gene expansion in P. pacificus would be especially helpful with respect to understanding the relatively minor phenotype of the Ppa-gcy-22.3 mutants.

In P. pacificus, there are 5 gcy-22-like paralogs and 3 gcy-7-like paralogs, which together form a subclade that is clearly distinct from the 1-1 Cel-gcy-22, Cel-gcy-5, and Cel-gcy-7 orthologs in a phylogenetic tree containing all rGCs in P. pacificus, C. elegans, and C. briggssae (Hong et al, eLife, 2019). In Ortiz et al (2006 and 2009), Cel-gcy-22 stands out from other ASER-type gcy genes (gcy-1, gcy-4, gcy-5) in being located on a separate chromosome (Chr. V) as well as in having a wider range of defects in chemoattraction towards salt ions. Given that the 5 P. pacificus gcy-22-like paralogs are located on 3 separate chromosomes without clear synteny to their C. elegans counterparts, it is likely that the gcy-22 paralogs emerged from independent and repeated gene duplication events after the separation of these Caenorhabditis and Pristionchus lineages. Our reporter strains for two other P. pacificus gcy-22-like paralogs either did not exhibit expression in amphid neurons (Ppa-gcy-22.1p::GFP, ) or exhibited expression in multiple neuron types in addition to a putative ASE neuron (Ppa-gcy-22.4p::GFP). We have expanded the discussion on the other P. pacificus gcy-22 paralogs.

(7) The calcium imaging data from Ppa-ASE is quite variable. It would be helpful to discuss this variability. It would also be helpful to clarify how the ASEL and ASER neurons are being conclusively identified during calcium imaging.

For each animal, the orientation of the nose and vulva were recorded and used as a guide to determine the ventral and dorsal sides of the worm, and subsequently, the left and right sides of the worm. Accounting for the plane of focus of the neuron pairs as viewed through the microscope, it was then determined whether the imaged neuron was the worm’s left or right neuron of each pair. We added this explanation to the Methods.

(8) More information about how the animals were treated prior to calcium imaging would be helpful. In particular, were they exposed to salt solutions prior to imaging? In addition, the animals are in an M9 buffer during imaging - does this affect calcium responses in Ppa-ASE and Ppa-AFD? More information about salt exposure, and how this affects neuron responses, would be very helpful.

Prior to calcium imaging, animals were picked from their cultivation plates (using an eyelash pick to minimize bacteria transfer) and placed in loading solution (M9 buffer with 0.1% Tween20 and 1.5 mM tetramisole hydrochloride, as indicated in the Method) to immobilize the animals until they were visibly completely immobilized.

(9) In Figure 6, the authors say that Ppa-gcy-22.3::GFP expression is absent in the Ppa-che1(ot5012) mutant. However, based on the figure, it looks like there is some expression remaining. Is there a residual expression of Ppa-gcy-22.3::GFP in ASE or possibly ectopic expression in AFD? Does Ppa-che-1 regulate rGC expression in AFD? It would be helpful to address the role of Ppa-che-1 in AFD neuron differentiation.

In Figure 6C, the green signal is autofluorescence in the gut, and there is no GFP expression detected in any of the 55 che-1(-) animals we examined. We are currently developing AFDspecific rGC markers (gcy-8 homologs) to be able to examine the role of Ppa-CHE-1 in regulating AFD identity.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Abstract: 'how does sensory diversity prevail within this neuronal constraint?' - could be clearer as 'numerical constraint' or 'neuron number constraint'.

We have clarified this passage as ‘…constraint in neuron number’.

(2) 'Sensory neurons in the Pristionchus pacificus' - should get rid of the 'the'.

We have removed the ‘the’.

(3) Figure 2: We have had some good results with the ALFA tag using a similar approach (tagging endogenous loci using CRISPR). I'm not sure if it is a Pristionchus thing, or if it is a result of our different protocols, but our staining appears stronger with less background. We use an adaptation of the Finney-Ruvkin protocol, which includes MeOH in the primary fixation with PFA, and overcomes the cuticle barrier with some LN2 cracking, DTT, then H2O2. No collagenase. If you haven't tested it already it might be worth comparing the next time you have a need for immunostaining.

We appreciate this suggestion. Our staining protocol uses paraformaldehyde fixation. We observed consistent and clear staining in only 4 neurons in CHE-1::ALFA animals but more background signals from TTX-1::ALFA in Figure 2I-J in that could benefit from improved immunostaining protocol.

(4) Page 6: 'By crossing the che-1 reporter transgene into a che-1 mutant background (see below), we also found that che-1 autoregulates its own expression (Figure 2F), as it does in C. elegans' - it took me some effort to understand this. It might make it easier for future readers if this is explained more clearly.

We understand this confusion and have changed the wording along with a supporting table with a more detailed account of che-1p::RFP expression in both ASE and AFD neurons in wildtype and che-1(-) backgrounds in the Results.

(5) Line numbers would make it easier for reviewers to reference the text.

We have added line numbers.

(6) Page 7: is 250mM NH₄Cl an ecologically relevant concentration? When does off-target/nonspecific activation of odorant receptors become an issue? Some discussion of this could help readers assess the relevance of the salt concentrations used.

This is a great question but one that is difficult to reconcile between experimental conditions that often use 2.5M salt as point-source to establish salt gradients versus ecologically relevant concentrations that are very heterogenous in salinity. Efforts to show C. elegans can tolerate similar levels of salinity between 0.20-0.30 M without adverse effects have been recorded previously (Hu et al., Analytica Chimica Acta 2015; Mah et al. Expedition 2017).

(7) It would be nice for readers to have a short orientation to the ecological relevance of the different salts - e.g. why Pristionchus has a particular taste for ammonium salts.

Pristionchus species are entomophilic and most frequently found to be associated with beetles in a necromenic manner. Insect cadavers could thus represent sources of ammonium in the soil. Additionally, ammonium salts could represent a biological signature of other nematodes that the predatory morphs of P. pacificus could interpret as prey. We have added the possible ecological relevance of ammonium salts into the Discussion.

(8) Page 11: 'multiple P. pacificus che-1p::GCaMP strains did not exhibit sufficient basal fluorescence to allow for image tracking and direct comparison'. 500ms exposure to get enough signal from RCaMP is slow, but based on the figures it still seems enough to capture things. If image tracking was the issue, then using GCaMP6s with SL2-RFP or similar in conjunction with a beam splitter enables tracking when the GCaMP signal is low. Might be an option for the future.

These are very helpful suggestions and we hope to eventually develop an improved che1p::GCaMP strain for future studies.

(9) Sometimes C. elegans genes are referred to as 'C. elegans [gene name]' and sometimes 'Cel [gene name]'. Should be consistent. Same with Pristionchus.

We have now combed through and corrected the inconsistencies in nomenclature.

(10) Pg 12 - '...supports the likelihood that AFD receives inputs, possibly neuropeptidergic, from other amphid neurons' - the neuropeptidergic part could do with some justification.

Because the AFD neurons are not exposed directly to the environment through the amphid channel like the ASE and other amphid neurons, the calcium responses to salts detected in the AFD likely originate from sensory neurons connected to the AFD. However, because there is no synaptic connection from other amphid neurons to the AFD neurons in P. pacificus (unlike in C. elegans; Hong et al, eLife, 2019), it is likely that neuropeptides connect other sensory neurons to the AFDs. To avoid unnecessary confusion, we have removed “possibly neuropeptidergic.”

(11) Pg16: the link to the Hallam lab codon adaptor has a space in the middle. Also, the paper should be cited along with the web address (Bryant and Hallam, 2021).

We have now added the proper link, plus in-text citation. https://hallemlab.shinyapps.io/Wild_Worm_Codon_Adapter/ (Bryant and Hallem, 2021)

Full citation:

Astra S Bryant, Elissa A Hallem, The Wild Worm Codon Adapter: a web tool for automated codon adaptation of transgenes for expression in non-Caenorhabditis nematodes, G3 Genes|Genomes|Genetics, Volume 11, Issue 7, July 2021, jkab146, https://doi.org/10.1093/g3journal/jkab146

Reviewer #2 (Recommendations for the authors):

(1) In Figure 1, the legend states that the population tested was "J4/L4 larvae and young adult hermaphrodites," whereas in the main text, the population was described as "adult hermaphrodites." Please clarify which ages were tested.

We have tested J4-Adult stage hermaphrodites and have made the appropriate corrections in the text.

(2) The authors state that "in contrast to C. elegans, we find that P. pacificus is only moderately and weakly attracted to NaCl and LiCl, respectively." However, this statement does not reflect the data shown in Figure 1, where there is no significant difference between C. elegans and P. pacificus - both species show at most weak attraction to NaCl.

Although there is no statistically significant difference in NaCl attraction between P. pacificus and C. elegans, NaCl attraction in P. pacificus is significantly lower than its attraction to all 3 ammonium salts when compared to C. elegans. We have rephrased this statement as relative differences in the Results and updated the Figure legend.

(3) In Figure 1, the comparisons between C. elegans and P. pacificus should be made using a two-way ANOVA rather than multiple t-tests. Also, the sample sizes should be stated (so the reader does not need to count the circles) and the error bars should be defined.

We performed the 2-way ANOVA to detect differences between C. elegans and P. pacificus for the same salt and between salts within each species. We also indicated the sample size on the figure and defined the error bars.

Significance:

For comparisons of different salt responses within the same species:

- For C. elegans, NH₄Br vs NH₄Cl (**p<0.01), NH₄Cl vs NH₄I (* p<0.05), and NH₄Cl vs NaCl (* p<0.05). All other comparisons are not significant.

- For P. pacificus, all salts showed (****p<0.0001) when compared to NaAc and to NH₄Ac, except for NH₄Ac and NaAc compared to each other (ns). Also, NH₄Cl showed (*p<0.05) and NH₄I showed (***p<0.001) when compared with LiCl and NaCl. All other comparisons are not significant.

For comparisons of salt responses between different species (N2 vs PS312):

- NH₄I and LiCl (*p<0.05); NaAc and NH₄Ac (****p<0.0001)

(4) It might be worth doing a power analysis on the data in Figure 3B. If the data are underpowered, this might explain why there is a difference in NH₄Br response with one of the null mutants but not the other.

For responses to NH₄Cl, since both che-1 mutants (rather than just one) showed significant difference compared to wildtype, we conducted a power analysis based on the effect size of that difference (~1.2; large). Given this effect size, the sample size for future experiments should be 12 (ANOVA).

For responses to NH₄Br and given the effect size of the difference seen between wildtype (PS312) and ot5012 (~0.8; large), the sample size for future experiments should be 18 (ANOVA) for a power value of 0.8. Therefore, it is possible that the sample size of 12 for the current experiment was too small to detect a possible difference between the ot5013 alleles and wildtype.

(5) It would be helpful to discuss why silencing Ppa-ASE might result in a switch from attractive to repulsive responses to some of the tested gustatory cues.

For similar assays using Ppa-odr-3p::HisCl1, increasing histamine concentration led to decreasing C.I. for a given odorant (myristate, a P. pacificus-specific attractant). It is likely that the amount of histamine treatment for knockdown to zero (i.e. without a valence change) will differ depending on the attractant.

(6) The statistical tests used in Figure 3 are not stated.

Figure 3 used Two-way ANOVA with Dunnett’s post hoc test. We have now added the test in the figure legend.

(7) It would be helpful to examine the responses of ASER to the full salt panel in the Ppa-gcy-22.3 vs. wild-type backgrounds.

We understand that future experiments examining neuron responses to the full salt panel for wildtype and gcy-22.3 mutants would provide further information about the salts and specific ions associated with the GCY-22.3 receptor. However, we have tested a broader range of salts (although not yet the full panel) for behavioral assays in wildtype vs gcy-22.3 mutants, which we have included as part of an added Figure 8.

(8) The controls shown in Figure S1 may not be adequate. Ideally, the same sample size would be used for the control, allowing differences between control worms and experimental worms to be quantified.

Although we had not conducted an equal number of negative controls using green light without salt stimuli due to resource constraints (6 control vs ~10-19 test), we provided individual recordings with stimuli to show that conditions we interpreted as having responses rarely showed responses resembling the negative controls. Similarly, those we interpreted as having no responses to stimuli mostly resembled the no-stimuli controls (e.g. WT to 25 mM NH₄Cl, gcy22.3 mutant to 250 mM NH₄Cl).

(9) An osmolarity control would be helpful for the calcium imaging experiments.

We acknowledge that future calcium imaging experiments featuring different salt concentrations could benefit from osmolarity controls.

(10) In Figure S7, more information about the microfluidic chip design is needed.

The chip design features a U-shaped worm trap to facilitate loading the worm head-first, with a tapered opening to ensure the worm fits snugly and will not slide too far forward during recording. The outer two chip channels hold buffer solution and can be switched open (ON) or closed (OFF) by the Valvebank. The inner two chip channels hold experimental solutions. The inner channel closer to the worm trap holds the control solution, and the inner channel farther from the worm trap holds the stimulant solution.

We have added an image of the chip in Figure S7 and further description in the legend.

(11) Throughout the manuscript, the discussion of the salt stimuli focuses on the salts more than the ions. More discussion of which ions are eliciting responses (both behavioral and neuronal responses) would be helpful.

In Figure 7, the gcy-22.3 defect resulted in a statistically significant reduction in response only towards NH₄Cl but not towards NaCl, which suggests ASER is the primary neuron detecting NH₄⁺ ions. To extend the description of the gcy-22.3 mutant defects to other ions, we have added a Figure 8: chemotaxis on various salt backgrounds. We found only a mild increase in attraction towards NH₄⁺ by both gcy-22.3 mutant alleles, but wild-type in their responses toward Cl^-, Na⁺, or I^-. The switch in the direction of change between the behavioral (enhanced) and calcium imaging result (reduced) suggests the behavioral response to ammonium ions likely involves additional receptors and neurons.

Minor comments:

(1) The full species name of "C. elegans" should be written out upon first use.

We have added ‘Caenorhabditis elegans’ to its first mention.

(2) In the legend of Figure 1, "N2" should not be in italics.

We have made the correction.

(3) The "che-1" gene should be in lowercase, even when it is at the start of the sentence.

We have made the correction.

(4) Throughout the manuscript, "HisCl" should be "HisCl1."

We have made these corrections to ‘HisCl1’.

(5) Figure 3A would benefit from more context, such as the format seen in Figure 7A. It would also help to have more information in the legend (e.g., blue boxes are exons, etc.).

(6) "Since NH₄I sensation is affected by silencing of che-1(+) neurons but is unaffected in che-1 mutants, ASE differentiation may be more greatly impacted by the silencing of ASE than by the loss of che-1": I don't think this is exactly what the authors mean. I would say, "ASE function may be more greatly impacted...".

We have changed ‘differentiation’ to ‘function’ in this passage.

(7) In Figure 7F-G, the AFD neurons are referred to as AFD in the figure title but AM12 in the graph. This is confusing.

Thank you for noticing this oversight. We have corrected “AM12” to “AFD”.

(8) In Figure 7, the legend suggests that comparisons within the same genotype were analyzed. I do not see these comparisons in the figure. In which cases were comparisons within the same genotype made?

Correct, we performed additional tests between ON and OFF states within the same genotypes (WT and mutant) but did not find significant differences. To avoid unnecessary confusion, we have removed this sentence.

(9) The nomenclature used for the transgenic animals is unconventional. For example, normally the calcium imaging line would be listed as csuEx93[Ppa-che-1p::optRCaMP] instead of Ppache-1p::optRCaMP(csuEx93).

We have made these corrections to the nomenclature.

(10) Figure S6 appears to come out of order. Also, it would be nice to have more of a legend for this figure. The format of the figure could also be improved for clarity.

We have corrected Figure S6 (now S8) and added more information to the legend.

(11) Methods section, Chemotaxis assays: "Most assays lasted ~3.5 hours at room temperature in line with the speed of P. pacificus without food..." It's not clear what this means. Does it take the worms 3.5 hours to crawl across the surface of the plate?

Correct, P. pacificus requires 3-4 hours to crawl across the surface of the plate, which is the standard time for chemotaxis assays for some odors and all salts. We have added this clarification to the Methods.

Author Response

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

eLife assessment

This study provides valuable insights into how the brain parses the syntactic structure of a spoken sentence. A unique contribution of the work is to use a large language model to quantify how the mental representation of syntactic structure updates as a sentence unfolds in time. Solid evidence is provided that distributive cortical networks are engaged for incremental parsing of a sentence, although the contribution could be further strengthened if the authors would further highlight the main results and clarify the benefit of using a large language model.

We thank the editors for the overall positive assessment. We have revised our manuscript to further emphasize our main findings and highlight the advantages of using a large language model (LLM) over traditional behavioural and corpus-based data.

This study aims to investigate the neural dynamics underlying the incremental construction of structured interpretation during speech comprehension. While syntactic cues play an important role, they alone do not define the essence of this parsing process. Instead, this incremental process is jointly determined by the interplay of syntax, semantics, and non-linguistic world knowledge, evoked by the specific words heard sequentially by listeners. To better capture these multifaceted constraints, we derived structural measures from BERT, which dynamically represent the evolving structured interpretation as a sentence unfolds word-by-word.

Typically, the syntactic structure of a sentence can be represented by a context-free parse tree, such as a dependency parse tree or a constituency-based parse tree, which abstracts away from specific content, assigning a discrete parse depth to each word regardless of its semantics. However, this context-free parse tree merely represents the result rather than the process of sentence parsing and does not elucidate how a coherent structured interpretation is concurrently determined by multifaceted constraints. In contrast, BERT parse depth, trained to approach the context-free discrete dependency parse depth, is a continuous variable. Crucially, its deviation from the corresponding discrete parse depth indicates the preference for the syntactic structure represented by this context-free parse. As BERT processes a sentence delivered word-by-word, the dynamic change of BERT parse depth reflects the incremental nature of online speech comprehension.

Our results reveal a behavioural alignment between BERT parse depth and human interpretative preference for the same set of sentences. In other words, BERT parse depth could represent a probabilistic interpretation of a sentence’s structure based on its specific contents, making it possible to quantify the preference for each grammatically correct syntactic structure during incremental speech comprehension. Furthermore, both BERT and human interpretations show correlations with linguistic knowledge, such as verb transitivity, and non-linguistic knowledge, like subject noun thematic role preference. Both types of knowledge are essential for achieving a coherent interpretation, in accordance with the “constraint-based hypothesis” of sentence processing.

Motivated by the observed behavioural alignment between BERT and human listeners, we further investigated BERT structural measures in source-localized EEG/MEG using representational similarity analyses (RSA). This approach revealed the neural dynamics underlying incremental speech comprehension on millisecond scales. Our main findings include: (1) a shift from bi-hemispheric lateral frontal-temporal regions to left-lateralized regions in representing the current structured interpretation as a sentence unfolds, (2) a pattern of sequential activations in the left lateral temporal regions, updating the structured interpretation as syntactic ambiguity is resolved, and (3) the influence of lexical interpretative coherence activated in the right hemisphere over the resolved sentence structure represented in the left hemisphere.

From our perspective, the advantages of using a LLM (or deep language model) like BERT are twofold. Conceptually, BERT structural measures offer a deep contextualized structural representation for any given sentence by integrating the multifaceted constraints unique to the specific contents described by the words within that sentence. Modelling this process on a word-by-word basis is challenging to achieve with behavioural or corpus-based metrics. Empirically, as demonstrated in our responses to the reviewers below, BERT measures show better performance compared to behavioural and corpus-based metrics in aligning with listeners’ neural activity. Moreover, when it comes to integrating multiple sources of constraints for achieving a coherent interpretation, BERT measures also show a better fit with the behavioural data of human listeners than corpus-based metrics.

Taken together, we propose that LLMs, akin to other artificial neural networks (ANNs), can be considered as computational models for formulating and testing specific neuroscientific hypotheses, such as the “constraint-based hypothesis” of sentence processing in this study. However, we by no means overlook the importance of corpus-based and behavioural metrics. These metrics play a crucial role in interpreting and assessing whether and how ANNs stimulate human cognitive processes, a fundamental step in employing ANNs to gain new insights into the neural mechanisms of human cognition.

Public Reviews:

Reviewer #1 (Public Review):

In this study, the authors investigate where and when brain activity is modulated by incoming linguistic cues during sentence comprehension. Sentence stimuli were designed such that incoming words had varying degrees of constraint on the sentence's structural interpretation as participants listened to them unfolding, i.e. due to varying degrees of verb transitivity and the noun's likelihood of assuming a specific thematic role. Word-by-word "online" structural interpretations for each sentence were extracted from a deep neural network model trained to reproduce language statistics. The authors relate the various metrics of word-by-word predicted sentence structure to brain data through a standard RSA approach at three distinct points of time throughout sentence presentation. The data provide convincing evidence that brain activity reflects preceding linguistic constraints as well as integration difficulty immediately after word onset of disambiguating material.

We thank Reviewer #1 (hereinafter referred to as R1) for their recognition of the objectives of our study and the analytical approaches we have employed in this study.

The authors confirm that their sentence stimuli vary in degree of constraint on sentence structure through independent behavioral data from a sentence continuation task. They also show a compelling correlation of these behavioral data with the online structure metric extracted from the deep neural network, which seems to pick up on the variation in constraints. In the introduction, the authors argue for the potential benefits of using deep neural networkderived metrics given that it has "historically been challenging to model the dynamic interplay between various types of linguistic and nonlinguistic information". Similarly, they later conclude that "future DLMs (...) may provide new insights into the neural implementation of the various incremental processing operations(...)".

We appreciate R1’s positive comments on the design, quantitative modelling and behavioural validation of the sentence stimuli used in this experiment.

By incorporating structural probing of a deep neural network, a technique developed in the field of natural language processing, into the analysis pipeline for investigating brain data, the authors indeed take an important step towards establishing advanced machine learning techniques for researching the neurobiology of language. However, given the popularity of deep neural networks, an argument for their utility should be carefully evidenced.

We fully concur with R1 regarding the need for cautious evaluation and interpretation of deep neural networks’ utility. In fact, this perspective underpinned our decision to conduct extensive correlation analyses using both behavioural and corpus-based metrics to make sense of BERT metrics. These analyses were essential to interpret and validate BERT metrics before employing them to investigate listeners’ neural activity during speech comprehension. We do not in any way undermine the importance of behavioural or corpus-based data in studying language processing in the brain. On the contrary, as evidenced by our findings, these traditional metrics are instrumental in interpreting and guiding the use of metrics derived from LLMs.

However, the data presented here don't directly test how large the benefit provided by this tool really is. In fact, the authors show compelling correlations of the neural network-derived metrics with both the behavioral cloze-test data as well as several (corpus-)derived metrics. While this is a convincing illustration of how deep language models can be made more interpretable, it is in itself not novel. The correlation with behavioral data and corpus statistics also raises the question of what is the additional benefit of the computational model? Is it simply saving us the step of not having to collect the behavioral data, not having to compute the corpus statistics or does the model potentially uncover a more nuanced representation of the online comprehension process? This remains unclear because we are lacking a direct comparison of how much variance in the neural data is explained by the neural network-derived metrics beyond those other metrics (for example the main verb probability or the corpusderived "active index" following the prepositional phrase).

From our perspective, a primary advantage of using the neural network-derived metrics (or LLMs as computational models of language processing), compared to traditional behavioural and corpus-based metrics, lies in their ability to offer more nuanced, contextualized representations of natural language inputs. There seems no effective way of computationally capturing the distributed and multifaceted constraints within specific contexts until the current generation of LLMs came along. While it is feasible to quantify lexical properties or contextual effects based on the usage of specific words via corpora or behavioural tests, this method appears less effective in modelling the composition of meanings across more words on the sentence level. More critically, it struggles with capturing how various lexical constraints collectively yield a coherent structured interpretation.

Accumulating evidence suggests that models designed for context prediction or next-word prediction, such as word2vec and LLMs, outperform classic count-based distributional semantic models (Baroni et al. 2014) in aligning with neural activity during language comprehension (Schrimpf et al. 2021; Caucheteux and King 2022). Relevant to this, we have conducted additional analyses to directly assess the additional variance of neural data explained by BERT metrics, over and above what traditional metrics account for. Specifically, using RSA, we re-tested model RDMs based on BERT metrics while controlling for the contribution from traditional metrics (via partial correlation).

During the first verb (V1) epoch, we tested model RDMs of V1 transitivity based on data from either the behavioural pre-test (i.e., continuations following V1) or massive corpora. Contrasting sharply with the significant model fits observed for BERT V1 parse depth in bilateral frontal and temporal regions, the two metrics of V1 transitivity did not exhibit any significant effects (see Author response image 1).

Author response image 1

RSA model fits of BERT structural metrics and behavioural/corpus-based metrics in the V1 epoch. (upper) Model fits of BERT V1 parse depth (relevant to Appendix 1-figure 10A); (middle) Model fits of the V1 transitivity based on the continuation pre-rest conducted at the end of V1 (e.g., completing “The dog found …”); (bottom) Model fits of the V1 transitivity based on the corpus data (as described in Methods). Note that verb transitivity is quantified as the proportion of its transitive uses (i.e., followed by a direct object) relative to its intransitive uses.

In the PP1 epoch, which was aligned to the onset of the preposition in the prepositional phrase (PP), we tested the probability of a PP continuation following V1 (e.g., the probability of a PP after “The dog found…”). While no significant results were found for PP probability, we have plotted the uncorrected results for PP probability (Author response image 2). These model fits have very limited overlap with those of BERT parse depth vector (up to PP1) in the left inferior frontal gyrus (approximately at 360 ms) and the left temporal regions (around 600 ms). It is noteworthy that the model fits of the BERT parse depth vector (up to PP1) remained largely unchanged even when PP probability was controlled for, indicating that the variance explained by BERT metrics cannot be effectively accounted for by the PP probability obtained from the human continuation pre-test.

Author response image 2

Comparison between the RSA model fits of BERT structural metrics and behavioural / corpusbased metrics in the PP1 epoch. (upper) Model fits of BERT parse depth vector up to PP1 (relevant to Figure 6B in the main text); (middle) Model fits of the probability of a PP continuation in the prerest conducted at the end of the first verb; (bottom) Model fits of BERT parse depth vector up to PP1 after partialling out the variance explained by PP probability.

Finally, in the main verb (MV) epoch, we tested the model RDM based on the probability of a MV continuation following the PP (e.g., the probability after “The dog found in the park…”). When compared with the BERT parse depth vector (up to MV), we observed a similar effect in the left dorsal frontal regions (see Author response image 3). However, this effect did not survive after the whole-brain multiple comparison correction. Subsequent partial correlation analyses revealed that the MV probability accounted for only a small portion of the variance in neural data explained by the BERT metric, primarily the effect observed in the left dorsal frontal regions around 380 ms post MV onset. Meanwhile, the majority of the model fits of the BERT parse depth vector remained largely unchanged after controlling for the MV probability.

Note that the probability of a PP/MV continuation reflect participants’ predictions based on speech input preceding the preposition (e.g., “The dog found…”) or the main verb (e.g., “The dog found in the park…”), respectively. In contrast, BERT parse depth vector is designed to represent the structure of the (partial) sentence in the speech already delivered to listeners, rather than to predict a continuation after it. Therefore, in the PP1 and MV epochs, we separately tested BERT parse depth vectors that included the preposition (e.g., “The dog found in…”) and the main verb (e.g., “The dog found in the park was…”) to accurately capture the sentence structure at these specific points in a sentence. Despite the differences in the nature of information captured by these two types of metrics, the behavioural metrics themselves did not exhibit significant model fits when tested against listeners’ neural activity.

Author response image 3

Comparison between the RSA model fits of BERT structural metrics and behavioural / corpusbased metrics in the MV epoch. (upper) Model fits of BERT parse depth vector up to MV (relevant to Figure 6C in the main text); (middle) Model fits of the probability of a MV continuation in the pre-rest conducted at the end of the prepositional phrase (e.g., “The dog found in the park …”); (bottom) Model fits of BERT parse depth vector up to MV after partialling out the variance explained by MV probability.

Regarding the corpus-derived interpretative preference, we observed that neither the Active index nor the Passive index showed significant effects in the PP1 epoch. In the MV epoch, while significant model fits of the passive index were observed, which temporally overlapped with the BERT parse depth vector (up to MV) after the recognition point of the MV, the effects of these two model RDMs emerged in different hemispheres, as illustrated in Figures 6C and 8D in the main text. Consequently, we opted not to pursue further partial correlation analysis with the corpus-derived interpretative preference. Besides, as shown in Figure 8A, 8B and 8C, subject noun thematic role preference and non-directional index exhibit significant model fits in the PP1 or the MV epoch. Interesting, these effects lead corresponding effects of BERT metrics in the same epoch (see Figure 6B and 6C), suggesting that the overall structured interpretation emerges after the evaluation and integration of multifaceted lexical constraints.

In summary, our findings indicate that, in comparison to corpus-derived or behavioural metrics, BERT structural metrics are more effective in explaining neural data, in terms of modelling both the unfolding sentence input (i.e., incremental BERT parse vector) and individual words (i.e., V1) within specific sentential contexts. This advantage of BERT metrics might be due to the hypothesized capacity of LLMs to capture more contextually rich representations. Such representations effectively integrate the diverse constraints present in a given sentence, thereby outperforming corpus-based metrics or behavioural metrics in this respect. Concurrently, it is important to recognize the significant role of corpus-based / behavioral metrics as explanatory variables. They are instrumental not only in interpreting BERT metrics but also in understanding their fit to listeners’ neural activity (by examining the temporal sequence and spatial distribution of model fits of these two types of metrics). Such an integrative approach allows for a more comprehensive understanding of the complex neural processes underpinning speech comprehension.

With regards to the neural data, the authors show convincing evidence for early modulations of brain activity by linguistic constraints on sentence structure and importantly early modulation by the coherence between multiple constraints to be integrated. Those modulations can be observed across bilateral frontal and temporal areas as well as parts of the default mode network. The methods used are clear and rigorous and allow for a detailed exploration of how multiple linguistic cues are neurally encoded and dynamically shape the final representation of a sentence in the brain. However, at times the consequences of the RSA results remain somewhat vague with regard to the motivation behind different metrics and how they differ from each other. Therefore, some results seem surprising and warrant further discussion, for example: Why does the neural network-derived parse depth metric fit neural data before the V1 uniqueness point if the sentence pairs begin with the same noun phrase? This suggests that the lexical information preceding V1, is driving the results. However, given the additional results, we can already exclude an influence of subject likelihood for a specific thematic role as this did not model the neural data in the V1 epoch to a significant degree.

As pointed out by R1, model fits of BERT parse depth vector (up to V1) and its mismatch for the active interpretation were observed before the V1 uniqueness point (Figures 6A and 6D). These early effects could be attributed to the inclusion of different subject nouns in the BERT parse depth vectors. In our MEG data analyses, RSA was performed using all LoTrans and HiTrans sentences. Each of the 60 sentence sets contained one LoTrans sentence and one HiTrans sentence, which resulted in a 120 x 120 neural data RDM for each searchlight ROI across the brain within each sliding time window. Although LoTrans and HiTrans sentences within the same sentence set shared the same subject noun, subject nouns varied across sentence sets. This variation was expected to be reflected in both the model RDM of BERT metrics and the data RDM, a point further clarified in the revised manuscript.

In contrast, when employing a model RDM constructed solely from the BERT V1 parse depth, we observed model fits peaking precisely at the uniqueness point of V1 (see Appendix 1figure 10). It is important to note that BERT V1 parse depth is a contextualized metric influenced by the preceding subject noun, which could account for the effects of BERT V1 parse depth observed before the uniqueness point of V1.

Relatedly, In Fig 2C it seems there are systematic differences between HiTrans and LoTrans sentences regarding the parse depth of determiner and subject noun according to the neural network model, while this is not expected according to the context-free parse.

We thank R1 for pointing out this issue. Relevant to Figure 3D (Figure 2C in the original manuscript), we presented the distributions of BERT parse depth for individual words as the sentence unfolds in Appendix 1-figure 2. Our analysis revealed that the parse depth of the subject noun in high transitivity (HiTrans) and low transitivity (LoTrans) sentences did not significantly differ, except for the point at which the sentence reached V1 (two-tailed twosample t-test, P = 0.05).

However, we observed a significant difference in the parse depth of the determiner between HiTrans and LoTrans sentences (two-tailed two-sample t-test, P < 0.05 for all results in Appendix 1-figure 2). Additionally, the parse depth of the determiner was found to covary with that of V1 as the input unfolded to different sentence positions (Pearson correlation, P < 0.05 for all plots in Appendix 1-figure 2). This difference, unexpected in terms of the contextfree (dependency) parse used for training the BERT structural probing model, might be indicative of a “leakage” of contextual information during the training of the structural probing model, given the co-variation between the determiner and V1 which was designed to be different in their transitivity in the two types of sentences.

Despite such unexpected differences observed in the BERT parse depths of the determiner, we considered the two sentence types as one group with distributed features (e.g., V1 transitivity) in the RSA, and used the BERT parse depth vector including all words in the sentence input to construct the model RDMs. Moreover, as indicated in Appendix 1-figure 3, compared to the content words, the determiner contributed minimally to the incremental BERT parse depth vector. Consequently, the noted discrepancies in BERT parse depth of the determiner between HiTrans and LoTrans sentences are unlikely to significantly bias our RSA results.

"The degree of this mismatch is proportional to the evidence for or against the two interpretations (...). Besides these two measures based on the entire incremental input, we also focused on Verb1 since the potential structural ambiguity lies in whether Verb1 is interpreted as a passive verb or the main verb." The neural data fits in V1 epoch differ in their temporal profile for the mismatch metrics and the Verb 1 depth respectively. I understand the "degree of mismatch" to be a measure of how strongly the neural network's hidden representations align with the parse depth of an active or passive sentence structure. If this is correct, then it is not clear from the text how far this measure differs from the Verb 1 depth alone, which is also indicating either an active or passive structure.

Within the V1 epoch, we tested three distinct types of model RDMs based on BERT metrics: (1) The BERT parse depth vector, representing the neural network’s hidden representation of the incremental sentence structure including all words up to V1. (2) The mismatch metric for either the Active or Passive interpretation, calculated as the distance between the BERT parse depth vector and the context-free parse depth vector for each interpretation. (3) The BERT parse depth of V1, crucial in representing the preferred structural interpretation of the unfolding sentence given its syntactic role as either a passive verb or the main verb.

While the BERT parse depth vector per se does not directly indicate a preferred interpretation, its mismatch with the context-free parse depth vectors of the two possible interpretations reveals the favoured interpretation, as significant neural fit is only anticipated for the mismatch with the interpretation being considered. The contextualized BERT depth of V1 is also indicative of the preferred structure given the context-free V1 parse depth corresponding to different syntactic roles, however, compared to the interpretative mismatch, it does not fully capture contributions from other words in the input. Consequently, we expected the interpretative mismatch and the BERT V1 depth to yield different results. Indeed, our analysis revealed that, although both metrics extracted from the same BERT layer (i.e., layer 13) demonstrated early RSA fits in the left fronto-temporal regions, the V1 depth showed relatively more prolonged effects with a notable peak occurring precisely at the uniqueness point of V1 (compare Figure 6C and Appendix 1-figure 10). These complementary results underscore the capability of BERT metrics to align with neural responses, in terms of both an incrementally unfolding sentence and a specific word within it.

In previous studies, differences in neural activity related to distinct amounts of open nodes in the parse tree have been interpreted in terms of distinct working memory demands (Nelson et al. pnas 2017, Udden et al tics 2020). It seems that some of the metrics, for example the neural network-derived parse depth or the V1 depth may be similarly interpreted in the light of working memory demands. After all, during V1 epoch, the sentences do not only differ with respect to predicted sentence structure, but also in the amount of open nodes that need to be maintained. In the discussion, however, the authors interpret these results as "neural representations of an unfolding sentence's structure".

We agree with the reviewer that the Active and Passive interpretations differ in terms of the number of open nodes before the actual main verb is heard. Given the syntactic ambiguity in our sentence stimuli (i.e., LoTrans and Hi Trans sentences), it is infeasible to determine the exact number of open nodes in each sentence as it unfolds. Nevertheless, the RSA fits observed in the dorsal lateral frontal regions could be indicative of the varying working memory demands involved in building the structured interpretations across sentences. We have added this perspective in the revised manuscript.

Reviewer #2 (Public Review):

This article is focused on investigating incremental speech processing, as it pertains to building higher-order syntactic structure. This is an important question because speech processing in general is lesser studied as compared to reading, and syntactic processes are lesser studied than lower-level sensory processes. The authors claim to shed light on the neural processes that build structured linguistic interpretations. The authors apply modern analysis techniques, and use state-of-the-art large language models in order to facilitate this investigation. They apply this to a cleverly designed experimental paradigm of EMEG data, and compare neural responses of human participants to the activation profiles in different layers of the BERT language model.

We thank Reviewer #2 (hereinafter referred to as R2) for the overall positive remarks on our study.

Strengths:

(1) The study aims to investigate an under-explored aspect of language processing, namely syntactic operations during speech processing

(2) The study is taking advantage of technological advancements in large language models, while also taking linguistic theory into account in building the hypothesis space

(3) The data combine EEG and MEG, which provides a valuable spatio-temporally resolved dataset

(4) The use of behavioural validation of high/low transitive was an elegant demonstration of the validity of their stimuli

We thank R2 for recognizing and appreciating the motivation and the methodology employed in this study.

Weaknesses:

(1) The manuscript is quite hard to understand, even for someone well-versed in both linguistic theory and LLMs. The questions, design, analysis approach, and conclusions are all quite dense and not easy to follow.

To address this issue, we have made dedicated efforts to clarify the key points in our study. We also added figures to visualize our experimental design and methods (see Figure 1, Figure 3C and Figure 5 in the revised main text). We hope that these revisions have made the manuscript more comprehensible and straightforward for the readers.

(2) The analyses end up seeming overly complicated when the underlying difference between sentence types is a simple categorical distinction between high and low transitivity. I am not sure why tree depth and BERT are being used to evaluate the degree to which a sentence is being processed as active or passive. If this is necessary, it would be helpful for the authors to motivate this more clearly.

Indeed, as pointed by R2, the only difference between LoTrans and HiTrans sentences is the first verb (V1), whose transitivity is crucial for establishing an initial preference for either an Active or a Passive interpretation as the sentence unfolds. Nonetheless, in line with the constraint-based approach to sentence processing and supported by previous research findings, a coherent structured interpretation of a sentence is determined by the combined constraints imposed by all words within that sentence. In our study, the transitivity of V1 alone is insufficient to fully explain the interpretative preference for the sentence structure. The overall sentence-level interpretation also depends on the thematic role preference of the subject noun – its likelihood of being an agent performing an action or a patient receiving the action.

This was evident in our findings, as shown in Author response image 1 above, where the V1 transitivity based on corpus or behavioural data did not fit to the neural data during the V1 epoch. In contrast, BERT structural measures [e.g., BERT parse depth vector (up to V1) and BERT V1 parse depth] offered contextualized representations that are presumed to integrate various lexical constraints present in each sentence. These BERT metrics exhibited significant model fits for the same neural data in the V1 epoch. Besides, a notable feature of BERT is its bi-directional attention mechanism, which allows for the dynamic updating of an earlier word’s representation as more of the sentence is heard, which is also changeling to achieve with corpus or behavioural metrics. For instance, the parse depth of the word “found” in the BERT parse depth vector for “The dog found…” differs from its parse depth in the vector for “The dog found in…”. This feature of BERT is particularly advantageous for investigating the dynamic nature of structured interpretation during speech comprehension, as it stimulates the continual updating of interpretation that occurs as a sentence unfolds (as shown by Figure 7 in the main text). We have elaborated on the rationale for employing BERT parse depth in this regard in the revised manuscript.

(3) The main data result figures comparing BERT and the EMEG brain data are hard to evaluate because only t-values are provided, and those, only for significant clusters. It would be helpful to see the full 600 ms time course of rho values, with error bars across subjects, to really be able to evaluate it visually. This is a summary statistic that is very far away from the input data

We appreciate this suggestion from R2. In the Appendix 1 of the revised manuscript, we have provided individual participants’ Spearman’s rho time courses for every model RDM tested in all the three epochs (see Appendix 1-figures 8-10 & 14-15). Note that RSA was conducted in the source-localized E/MEG, it is infeasible to plot the rho time course for each searchlight at one of the 8196 vertices on the cortical surface mesh. Instead, we plotted the rho time course of each ROI reported in the original manuscript. These plots complement the time-resolved heatmap of peak t-value in Figures 6-8 in the main text.

(4) Some details are omitted or not explained clearly. For example, how was BERT masked to give word-by-word predictions? In its default form, I believe that BERT takes in a set of words before and after the keyword that it is predicting. But I assume that here the model is not allowed to see linguistic information in the future.

In our analyses, we utilized the pre-trained version of BERT (Devlin et al. 2019) as released by Hugging Face (https://github.com/huggingface). It is noteworthy that BERT, as described in the original paper, was initially trained using the Cloze task, involving the prediction of masked words within an input. In our study, however, we neither retrained nor fine-tuned the pre-trained BERT model, nor did we employ it for word-by-word prediction tasks. We used BERT to derive the incremental representation of a sentence’s structure as it unfolded word-by-word.

Specifically, we sequentially input the text of each sentence into the BERT, akin to how a listener would receive the spoken words in a sentence (see Figure 3C in the main text). For each incremental input (such as “The dog found”), we extracted the hidden representations of each word from BERT. These representations were then transformed into their respective BERT parse depths using a structural probing model (which was trained using sentences with annotated dependency parse tress from the Penn Treebank Dataset). The resulting BERT parse depths were subsequently used to create model RDMs, which were then tested against neural data via RSA.

Crucially, in our approach, BERT was not exposed to any future linguistic information in the sentence. We never tested BERT parse depth of a word in an epoch where this word had not been heard by the listener. For example, the three-dimensional BERT parse depth vector for “The dog found” was tested in the V1 epoch corresponding to “found”, while the fourdimensional BERT parse depth vector for “The dog found in” was tested in the PP1 epoch of “in”.

How were the auditory stimuli recorded? Was it continuous speech or silences between each word? How was prosody controlled? Was it a natural speaker or a speech synthesiser?

Consistent with our previous studies (Kocagoncu et al. 2017; Klimovich-Gray et al. 2019; Lyu et al. 2019; Choi et al. 2021), all auditory stimuli in this study were recorded by a female native British English speaker, ensuring a neutral intonation throughout. We have incorporated this detail into the revised version of our manuscript for clarity.

It is difficult for me to fully assess the extent to which the authors achieved their aims, because I am missing important information about the setup of the experiment and the distribution of test statistics across subjects.

We are sorry for the previously omitted details regarding the experimental setup and the results of individual participants. As detailed in our responses above, we have now included the necessary information in the revised manuscript.

Reviewer #3 (Public Review):

Syntactic parsing is a highly dynamic process: When an incoming word is inconsistent with the presumed syntactic structure, the brain has to reanalyze the sentence and construct an alternative syntactic structure. Since syntactic parsing is a hidden process, it is challenging to describe the syntactic structure a listener internally constructs at each time moment. Here, the authors overcome this problem by (1) asking listeners to complete a sentence at some break point to probe the syntactic structure mentally constructed at the break point, and (2) using a DNN model to extract the most likely structure a listener may extract at a time moment. After obtaining incremental syntactic features using the DNN model, the authors analyze how these syntactic features are represented in the brain using MEG.

We extend our thanks to Reviewer #3 (referred to as R3 below) for recognizing the methods we used in this study.

Although the analyses are detailed, the current conclusion needs to be further specified. For example, in the abstract, it is concluded that "Our results reveal a detailed picture of the neurobiological processes involved in building structured interpretations through the integration across multifaceted constraints". The readers may remain puzzled after reading this conclusion.

Following R3’s suggestion, we have revised the abstract and refined our conclusions in the main text to explicitly highlight our principal findings. These include: (1) a shift from bihemispheric lateral frontal-temporal regions to left-lateralized regions in representing the current structured interpretation as a sentence unfolds, (2) a pattern of sequential activations in the left lateral temporal regions, updating the structured interpretation as syntactic ambiguity is resolved, and (3) the influence of lexical interpretative coherence activated in the right hemisphere over the resolved sentence structure represented in the left hemisphere.

Similarly, for the second part of the conclusion, i.e., "including an extensive set of bilateral brain regions beyond the classical fronto-temporal language system, which sheds light on the distributed nature of language processing in the brain." The more extensive cortical activation may be attributed to the spatial resolution of MEG, and it is quite well acknowledged that language processing is quite distributive in the brain.

We fully agree with R3 on the relatively low spatial resolution of MEG. Our emphasis was on the observed peak activations in specific regions outside the classical brain areas related to language processing, such as the precuneus in the default mode network, which are unlikely to be artifacts due to the spatial resolution of MEG. We have revised the relevant contents in the Abstract.

The authors should also discuss:

(1) individual differences (whether the BERT representation is a good enough approximation of the mental representation of individual listeners).

To address the issue of individual differences which was also suggested by R2, we added individual participants’ model fits in ROIs with significant effects of BERT representations in Appendix 1 of the revised manuscript (see Appendix 1-figures 8-10 & 14-15).

(2) parallel parsing (I think the framework here should allow the brain to maintain parallel representations of different syntactic structures but the analysis does not consider parallel representations).

In the original manuscript, we did not discuss parallel parsing because the methods we used does not support a direct test for this hypothesis. In our analyses, we assessed the preference for one of two plausible syntactic structures (i.e., Active and Passive interpretations) based on the BERT parse vector of an incremental sentence input. This assessment was accomplished by calculating the mismatch between the BERT parse depth vector and the context-free dependency parse depth vector representing each of the two structures. However, we only observed one preferred interpretation in each epoch (see Figures 6D-6F) and did not find evidence supporting the maintenance of parallel representations of different syntactic structures in the brain. Nevertheless, in the revised manuscript, we have mentioned this possibility, which could be properly explored in future studies.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Consider fitting the behavioral data from the continuation pre-test to the brain data in order to illustrate the claimed advantage of using a computational model beyond more traditional methods.

Following R1’s suggestion, we conducted additional RSA using more behavioural and corpusbased metrics. We then directly compared the fits of these traditional metrics to brain data with those of BERT metrics in the same epoch to provide empirical evidence for the advantage of using a computational model like BERT to explain listeners’ neural data (see Appendix 1figures 11-13).

Clarify the use of "neural representations: For a clearer assessment of the results, please discuss your results (especially the fits with BERT parse depth) in terms of the potential effects of distinct sentence structure expectations on working memory demands and make clear where these can be disentangled from neural representations of an unfolding sentence's structure.

In the revised manuscript, we have noted the working memory demands associated with the online construction of a structured interpretation during incremental speech comprehension. As mentioned in our response to the relevant comment by R1 above, our experimental paradigm is not suitable for quantitatively assessing working memory demands since it is difficult to determine the exact number of open nodes for our stimuli with syntactic ambiguity before the disambiguating point (i.e., the main verb) is reached. Therefore, while we can speculate the potential contribution of varying working memory demands (which might correlate with BERT V1 parse depth) to RSA model fits, we think it is not possible to disentangle their effects from the neural representation of an unfolding sentence’s structure modelled by BERT parse depths in our current study.

Please add in methods a description of how the uniqueness point was determined.

In this study, we defined the uniqueness point of a word as the earliest point in time when this word can be fully recognized after removing all of its phonological competitors. To determine the uniqueness point for each word of interest, we first identified the phoneme by which this word can be uniquely recognized according to CELEX (Baayen et al. 1993). Then, we manually labelled the offset of this phoneme in the auditory file of the spoken sentence in which this word occurred. We have added relevant description of how the uniqueness point was determined in the Methods section of the revised manuscript.

I found the name "interpretative mismatch" very opaque. Maybe instead consider "preference".

We chose to use the term “interpretative mismatch” rather than “preference” based on the operational definition of this metric, which is the distance between a BERT parse depth vector and one of the two context-free parse depth vectors representing the two possible syntactic structures, so that a smaller distance value (or mismatch) signifies a stronger preference for the corresponding interpretation.

In the abstract, the authors describe the cognitive process under investigation as one of incremental combination subject to "multi-dimensional probabilistic constraint, including both linguistic and non-linguistic knowledge". The non-linguistic knowledge is later also referred to as "broad world knowledge". These terms lack specificity and across studies have been operationalized in distinct ways. In the current study, this "world knowledge" is operationalized as the likelihood of a subject noun being an agent or patient and the probability for a verb to be transitive, so here a more specific term may have been the "knowledge about statistical regularities in language".

In this study, we specifically define “non-linguistic world knowledge” as the likelihood of a subject noun assuming the role of an agent or patient, which relates to its thematic role preference. This type of knowledge is primarily non-linguistic in nature, as exemplified by comparing nouns like “king” and “desk”. Although it could be reflected by statistical regularities in language, thematic role preference hinges more on world knowledge, plausibility, or real-world statistics. In contrast, “linguistic knowledge” in our study refers to verb transitivity, which focuses on the grammatically correct usage of a verb and is tied to statistical regularities within language itself. In the revised manuscript, we have provided clearer operational definitions for these two concepts and have ensured consistent usage throughout the text.

Please spell out what exactly the "constraint-based hypothesis" is (even better, include an explicit description of the alternative hypothesis?).

The “constraint-based hypothesis”, as summarized in a review (McRae and Matsuki 2013), posits that various sources of information, referred to as “constraints”, are simultaneously considered by listeners during incremental speech comprehension. These constraints encompass syntax, semantics, knowledge of common events, contextual pragmatic biases, and other forms of information gathered from both intra-sentential and extra-sentential context. Notably, there is no delay in the utilization of these multifaceted constraints once they become available, neither is a fixed priority assigned to one type of constraint over another. Instead, a diverse set of constraints is immediately brought into play for comprehension as soon as they become available as the relevant spoken word is recognized.

An alternative hypothesis, proposed earlier, is the two-stage garden path model (Frazier and Rayner 1982; Frazier 1987). According to this model, there is an initial parsing stage that relies solely on syntax. This is followed by a second stage where all available information, including semantics and other knowledge, is used to assess the plausibility of the results obtained in the first-stage analysis and to conduct re-analysis if necessary (McRae and Matsuki 2013). In the Introduction of our revised manuscript, we have elaborated on the “constraint-based hypothesis” and mentioned this two-stage garden path model as its alternative.

Fig1 B&C: In order to make the data more interpretable, could you estimate how many possible grammatical structural configurations there are / how many different grammatical structures were offered in the pretest, and based on this what would be the "chance probability" of choosing a random structure or for example show how many responded with a punctuation vs alternative continuations?

In our analysis of the behavioural results, we categorized the continuations provided by participants in the pre-test at the offset of Verb1 (e.g., “The dog found/walked …”) into 6 categories, including DO (direct object), INTRANS (intransitive), PP (prepositional phrase), INF (infinitival complement), SC (sentential complement) and OTHER (gerund, phrasal verb, etc.).

Author response table 1.

Similarly, we categorized the continuations that followed the offset of the prepositional phrase (e.g., “The dog found/walked in the park …”) into 7 categories, including MV (main verb), END (i.e., full stop), PP (prepositional phrase), INF (infinitival complement), CONJ (conjunction), ADV (adverb) and OTHER (gerund, sentential complement, etc.).

Author response table 2.

It is important to note that the results of these two pre-tests, including the types of continuations and their probabilities, exhibited considerable variability between and within each sentence type (see also Figures 2B and 2C).

Typo: "In addition, we found that BERT structural interpretations were also a correlation with the main verb probability" >> correlated instead of correlation.

We apologize for this typo. We have conducted a thorough proofreading to identify and correct any other typos present in the revised manuscript.

"In this regard, DLMs excel in a flexible combination of different types of features embedded in their rich internal representations". What are the "different types", spell out at least some examples for illustration.

We have rephrased this sentence to give a more detailed description.

Fig 2 caption: "Same color scheme as in (A)" >> should be 'as in (B)'?, and later A instead of B.

We are sorry for this typo. We have corrected it in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

My biggest recommendation is to make the paper clearer in two ways: (i) writing style, by hand-holding the reader through each section, and the motivation for each step, in both simple and technical language; (ii) schematic visuals, of the experimental design and the analysis. A schematic of the main experimental manipulation would be helpful, rather than just listing two example sentences. It would also be helpful to provide a schematic of the experimental setup and the analysis approach, so that people can refer to a visual aid in addition to the written explanation. For example, it is not immediately clear what is being correlated with what - I needed to go to the methods to understand that you are doing RSA across all of the trials. Make sure that all of the relevant details are explained, and that you motivate each decision.

We thank R2 for these suggestions. In the revised manuscript, we have enhanced the clarity of the main text by providing a more detailed explanation of the motivation behind each analysis and the interpretation of the corresponding results. Additionally, in response to R2’s recommendation, we have added a few figures, including the illustration of the experimental design (Figure 1) and methods (see Figure 3C and Figure 5).

Different visualisation of neural results - The main data result figures comparing BERT and the EMEG brain data are hard to evaluate because only t-values are provided, and those, are only for significant clusters. It would be helpful to see the full 600 ms time course of rho values, with error bars across subjects, to really be able to evaluate it visually.

In the original manuscript, we opted to present t-value time courses for the sake of simplicity in illustrating the fits of the 12 model RDMs tested in 3 epochs. Following R2’s suggestion, we have included the ROI model fit time courses of each model RDM for all individual participants, as well as the mean model fit time course with standard error in Appendix 1figures 8-10 & 14-15.

How are the authors dealing with prosody differences that disambiguate syntactic structures, that BERT does not have access to?

All spoken sentence stimuli were recorded by a female native British English speaker, ensuring a neutral intonation throughout. Therefore, prosody is unlikely to vary systematically between different sentence types or be utilized to disambiguate syntactic structures. Sample speech stimuli have been made available in the following repository: https://osf.io/7u8jp/.

A few writing errors: "was kept updated every time"

We are sorry for the typos. We have conducted proof-reading carefully to identify and correct typos throughout the revised manuscript.

Explain why the syntactic trees have "in park the" rather than "in the park"?

The dependency parse trees (e.g., Figure 3A) were generated according to the conventions of dependency parsing (de Marneffe et al. 2006).

Why are there mentions of the multiple demand network in the results? I'm not sure where this comes from.

The mention of the multiple demand network was made due to the significant RSA fits observed in the dorsal lateral prefrontal regions and the superior parietal regions, which are parts of the multiple demand network. This observation was particularly notable for the BERT parse depth vector in the main verb epoch when the potential syntactic ambiguity was being resolved. It is plausible that these effects observed are partly attributed to the varying working memory demands required to maintain the “opening nodes” in the different syntactic structures being considered by listeners at this point in the sentence.

Reviewer #3 (Recommendations For The Authors):

The study first asked human listeners to complete partial sentences, and incremental parsing of the partial sentences can be captured based on the completed sentences. This analysis is helpful and I wonder if the behavioral data here are enough to model the E/MEG responses. For example, if I understood it correctly, the parse depth up to V1 can be extracted based on the completed sentences and used for the E/MEG analysis.

The behavioural data alone do not suffice to model the E/MEG data. As we elucidated in our responses to R1, we employed three behavioural metrics derived from the continuation pretests. These metrics include the V1 transitivity and the PP probability, given the continuations after V1 (e.g., after “The dog found…”), as well as the MV probability, given the continuations after the prepositional phrase (e.g., after “The dog found in the park…”). These metrics aimed to capture participants’ prediction based on their structured interpretations at various positions in the sentence. However, none of these behavioural metrics yielded significant model fits to the listeners’ neural activity, which sharply contrasts with the substantial model fits of the BERT metrics in the same epochs. Besides, we also tried to model V1 parse depth as a weighted average based on participants’ continuations. As shown in Figure 3A, V1 parse depth is 0 in the active interpretation, 2 in the passive interpretation, while the parse depth of the determiner and the subject noun does not differ. However, this continuation-based V1 parse depth [i.e., 0 × Probability(active interpretation) + 2 × Probability(passive interpretation)] did not show significant model fits.

Related to this point, I wonder if the incremental parse extracted using BERT is consistent with the human results (i.e., parsing extracted based on the completed sentences) on a sentence-bysentence basis.

In fact, we did provide evidence showing the alignment between the incremental parse extracted using BERT and the human interpretation for the same partial sentence input (see Figure 4 in the main text and Appendix 1-figures 4-6).

Furthermore, in Fig 1d, is it possible to calculate how much variance of the 3 probabilities is explained by the 4 factors, e.g., using a linear model? If these factors can already explain most of the variance of human parsing, is it possible to just use these 4 factors to explain neural activity?

Following R3’s suggestion, we have conducted additional linear modelling analyses to compare the extent to which human behavioural data can be explained by corpus metrics and BERT metrics separately. Specifically, for each of the three probabilities obtained in the pretests (i.e., DO, PP, and MV), we constructed two linear models. One model utilized the four corpus-based metrics as regressors (i.e., SN agenthood, V1 transitivity, Passive index, and Active index), while the other model used BERT metrics as regressors (i.e., BERT parse depth of each word up to V1 from layer 13 for DO/PP probability and BERT parse depth of each word up to the end of PP from layer 14 for MV probability, consistent with the BERT layers reported in Figure 6).

As shown in the table below, corpus metrics demonstrate a more effective fit than BERT metrics for predicting the DO/PP probability. The likelihood of a DO/PP continuation is chiefly influenced by the lexical syntactic property of V1 (i.e., transitivity), and appears to rely less on contextual factors. Since V1 transitivity is explicitly included as one of the corpus metrics, it is thus expected to align more closely with the DO/PP probability compared to BERT metrics, primarily reflecting transitive versus intransitive verb usage.

Author response table 3.

Actually, BERT V1 parse depth was not correlated with V1 transitivity when the sentence only unfolds to V1 (see Appendix 1-figure 6). This lack of correlation may stem from the fact that the BERT probing model was designed to represent the structure of a (partially) unfolded sentence, rather than to generate a continuation or prediction. Moreover, V1 transitivity alone does not conclusively determine the Active or Passive interpretation by the end of V1. For instance, both transitive and intransitive continuations after V1 are compatible with an Active interpretation. Consequently, the initial preference for an Active interpretation (as depicted by the early effects before V1 was recognized in Figure 6D), might be predominantly driven by the animate subject noun (SN) at the beginning of the sentence, a word order cue in languages like English (Mahowald et al. 2023).

In contrast, when assessing the probability of a MV following the PP (e.g., after “The dog found in the park ...”), BERT metrics significantly outperformed corpus metrics in terms of fitting the MV probability. Although SN thematic role preference and V1 transitivity were designed to be the primary factors constraining the structured interpretation in this experiment, we could only obtain their context-independent estimates from corpora (i.e., considering all contexts). Additionally, despite Active/Passive index (a product of these two factors) are correlated with the MV probability, it may oversimplify the task of capturing the specific context of a given sentence. Furthermore, the PP following V1 is also expected to influence the structured interpretation. For instance, whether “in the park” is a more plausible scenario for people to find a dog or for a dog to find something. Thus, this finding suggests that the corpus-based metrics are not as effective as BERT in representing contextualized structured interpretations (for a longer sentence input), which might require the integration of constraints from every word in the input.

In summary, corpus-based metrics excel in explaining human language behaviour when it primarily relies on specific lexical properties. However, they significantly lag behind BERT metrics when more complex contextual factors come into play at the same time. Regarding their performance in fitting neural data, among the four corpus-based metrics, we only observed significant model fits for the Passive index in the MV epoch when the intended structure for a Passive interpretation was finally resolved, while the other three metrics did not exhibit significant model fits in any epoch. Note that subject noun thematic role preference did fit neural data in the PP and MV epochs (Figure 8A and 8B). In contrast, the incremental BERT parse depth vector exhibited significant model fits in all three epochs we tested (i.e., V1, PP1, and MV).

To summarize, I feel that I'm not sure if the structural information BERT extracts reflect the human parsing of the sentences, especially when the known influencing factors are removed.

Based on the results presented above and, in the manuscript, BERT metrics align closely with human structured interpretations in terms of both behavioural and neural data. Furthermore, they outperform corpus-based metrics when it comes to integrating multiple constraints within the context of a specific sentence as it unfolds.

Minor issues:

Six types of sentences were presented. Three types were not analyzed, but the results for the UNA sentences are not reported either.

In this study, we only analysed two out of the six types of sentences, i.e., HiTrans and LoTrans sentences. The remaining four types of sentences were included to ensure a diverse range of sentence structures and avoid potential adaption the same syntactic structure.

Fig 1b, If I understood it correctly, each count is a sentence. Providing examples of the sentences may help. Listing the sentences with the corresponding probabilities in the supplementary materials can also help.

Yes, each count in Figure 2B (Figure 1B in the original manuscript) is a sentence. All sentence stimuli and results of pre-tests are available in the following repository https://osf.io/7u8jp/.

"trajectories of individual HiTrans and LoTrans sentences are considerably distributed and intertwined (Fig. 2C, upper), suggesting that BERT structural interpretations are sensitive to the idiosyncratic contents in each sentence." It may also mean the trajectories are noisy.

We agree with R3 that there might be unwanted noise underlying the distributed and intertwined BERT parse depth trajectories of individual sentences. Meanwhile, it is also important to note that the correlation between BERT parse depths and lexical constraints of different words at the same position across sentences is statistically supported.

References

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Author response:

The following is the authors’ response to the original reviews

We thank the reviewers for their careful reading of our manuscript and their considered feedback. Please see our detailed response to reviewer comments inset below.

In addition to requested modifications we have also uploaded the proteomics data from 2 of the experiments contained within the manuscript onto the Immunological Proteome Resource (ImmPRes) website: immpres.co.uk making the data available in an easy-to-use graphical format for interested readers to interrogate and explore. We have added the following text to the data availability section (lines 1085-1091) to indicate this:

“An easy-to-use graphical interface for examining protein copy number expression from the 24-hour TCR WT and Pim dKO CD4 and CD8 T cell proteomics and IL-2 and IL-15 expanded WT and Pim dKO CD8 T cell proteomics datasets is also available on the Immunological Proteome Resource website: immpres.co.uk (Brenes et al., 2023) under the Cell type(s) selection: “T cell specific” and Dataset selection: “Pim1/2 regulated TCR proteomes” and “Pim1/2 regulated IL2 or IL15 CD8 T cell proteomes”.”

As well as indicating in figure legends where proteomics datasets are first introduced in Figures 1, 2 and 4 with the text:

“An interactive version of the proteomics expression data is available for exploration on the Immunological Proteome Resource website: immpres.co.uk”

Public Reviews:

Reviewer #1 (Public Review):

Summary and Strengths:

The study focuses on PIM1 and 2 in CD8 T cell activation and differentiation. These two serine/threonine kinases belong to a large network of Serine/Threonine kinases that acts following engagement of the TCR and of cytokine receptors and phosphorylates proteins that control transcriptional, translational and metabolic programs that result in effector and memory T cell differentiation. The expression of PIM1 and PIM2 is induced by the T-cell receptor and several cytokine receptors. The present study capitalized on high-resolution quantitative analysis of the proteomes and transcriptomes of Pim1/Pim2-deficient CD8 T cells to decipher how the PIM1/2 kinases control TCRdriven activation and IL-2/IL-15-driven proliferation, and differentiation into effector T cells.

Quantitative mass spectrometry-based proteomics analysis of naïve OT1 CD8 T cell stimulated with their cognate peptide showed that the PIM1 protein was induced within 3 hours of TCR engagement, and its expression was sustained at least up to 24 hours. The kinetics of PIM2 expression was protracted as compared to that of PIM1. Such TCRdependent expression of PIM1/2 correlated with the analysis of both Pim1 and Pim2 mRNA. In contrast, Pim3 mRNA was only expressed at very low levels and the PIM3 protein was not detected by mass spectrometry. Therefore, PIM1 and 2 are the major PIM kinases in recently activated T cells. Pim1/Pim2 double knockout (Pim dKO) mice were generated on a B6 background and found to express a lower number of splenocytes. No difference in TCR/CD28-driven proliferation was observed between WT and Pim dKO T cells over 3 days in culture. Quantitative proteomics of >7000 proteins further revealed no substantial quantitative or qualitative differences in protein content or proteome composition. Therefore, other signaling pathways can compensate for the lack of PIM kinases downstream of TCR activation.

Considering that PIM1 and PIM2 kinase expression is regulated by IL-2 and IL-15, antigen-primed CD8 T cells were expanded in IL-15 to generate memory phenotype CD8 T cells or expanded in IL-2 to generate effector cytotoxic T lymphocytes (CTL). Analysis of the survival, proliferation, proteome, and transcriptome of Pim dKO CD8 T cells kept for 6 days in IL-15 showed that PIM1 and PIM2 are dispensable to drive the IL-15mediated metabolic or differentiation programs of antigen-primed CD8 T cells. Moreover, Pim1/Pim2-deficiency had no impact on the ability of IL-2 to maintain CD8 T cell viability and proliferation. However, WT CTL downregulated the expression of CD62L whereas the Pim dKO CTL sustained higher CD62L expression. Pim dKO CTL was also smaller and less granular than WT CTL. Comparison of the proteome of day 6 IL-2 cultured WT and Pim dKO CTL showed that the latter expressed lower levels of the glucose transporters, SLC2A1 and SLC2A3, of a number of proteins involved in fatty acid and cholesterol biosynthesis, and CTL effector proteins such as granzymes, perforin, IFNg, and TNFa. Parallel transcriptomics analysis showed that the reduced expression of perforin and some granzymes correlated with a decrease in their mRNA whereas the decreased protein levels of granzymes B and A, and the glucose transporters SLC2A1 and SLC2A3 did not correspond with decreased mRNA expression. Therefore, PIM kinases are likely required for IL-2 to maximally control protein synthesis in CD8 CTL. Along that line, the translational repressor PDCD4 was increased in Pim dKO CTL and pan-PIM kinase inhibitors caused a reduction in protein synthesis rates in IL-2expanded CTL. Finally, the differences between Pim dKO and WT CTL in terms of CD62L expression resulted in Pim dKO CTL but not WT CTL retained the capacity to home to secondary lymphoid organs. In conclusion, this thorough and solid study showed that the PIM1/2 kinases shape the effector CD8 T cell proteomes rather than transcriptomes and are important mediators of IL2-signalling and CD8 T cell trafficking.

Weaknesses:

None identified by this reviewer.

Reviewer #2 (Public Review):

Summary:

Using a suite of techniques (e.g., RNA seq, proteomics, and functional experiments ex vivo) this paper extensively focuses on the role of PIM1/2 kinases during CD8 T-cell activation and cytokine-driven (i.e., IL-2 or IL-15) differentiation. The authors' key finding is that PIM1/2 enhances protein synthesis in response to IL-2 stimulation, but not IL-15, in CD8+ T cells. Loss of PIM1/2 made T cells less 'effector-like', with lower granzyme and cytokine production, and a surface profile that maintained homing towards secondary lymphoid tissue. The cytokines the authors focus on are IL-15 and Il-2, which drive naïve CD8 T cells towards memory or effector states, respectively. Although PIM1/2 are upregulated in response to T-cell activation and cytokine stimulation (e.g., IL-15, and to a greater extent, IL-2), using T cells isolated from a global mouse genetic knockout background of PIM1/2, the authors find that PIM1/2 did not significantly influence T-cell activation, proliferation, or expression of anything in the proteome under anti-

CD3/CD28 driven activation with/without cytokine (i.e., IL-15) stimulation ex vivo. This is perhaps somewhat surprising given PIM1/2 is upregulated, albeit to a small degree, in response to IL-15, and yet PIM1/2 did not seem to influence CD8+ T cell differentiation towards a memory state. Even more surprising is that IL-15 was previously shown to influence the metabolic programming of intestinal intraepithelial lymphocytes, suggesting cell-type specific effects from PIM kinases. What the authors went on to show, however, is that PIM1/2 KO altered CD8 T cell proteomes in response to IL-2. Using proteomics, they saw increased expression of homing receptors (i.e., L-selectin, CCR7), but reduced expression of metabolism-related proteins (e.g., GLUT1/3 & cholesterol biosynthesis) and effector-function related proteins (e.g., IFNy and granzymes). Rather neatly, by performing both RNA-seq and proteomics on the same IL2 stimulated WT vs. PIM1/2 KO cells, the authors found that changes at the proteome level were not corroborated by differences in RNA uncovering that PIM1/2 predominantly influence protein synthesis/translation. Effectively, PIM1/2 knockout reduced the differentiation of CD8+ T cells towards an effector state. In vivo adoptive transfer experiments showed that PIM1/2KO cells homed better to secondary lymphoid tissue, presumably owing to their heightened L-selectin expression (although this was not directly examined).

Strengths:

Overall, I think the paper is scientifically good, and I have no major qualms with the paper. The paper as it stands is solid, and while the experimental aim of this paper was quite specific/niche, it is overall a nice addition to our understanding of how serine/threonine kinases impact T cell state, tissue homing, and functionality. Of note, they hint towards a more general finding that kinases may have distinct behaviour in different T-cell subtypes/states. I particularly liked their use of matched RNA-seq and proteomics to first suggest that PIM1/2 kinases may predominantly influence translation (then going on to verify this via their protein translation experiment - although I must add this was only done using PIM kinase inhibitors, not the PIM1/2KO cells). I also liked that they used small molecule inhibitors to acutely reduce PIM1/2 activity, which corroborated some of their mouse knockout findings - this experiment helps resolve any findings resulting from potential adaptation issues from the PIM1/2 global knockout in mice but also gives it a more translational link given the potential use of PIM kinase inhibitors in the clinic. The proteomics and RNA seq dataset may be of general use to the community, particularly for analysis of IL-15 or IL-2 stimulated CD8+ T cells.

We thank the reviewer for their comments supporting the robustness and usefulness of our data.

Weaknesses:

It would be good to perform some experiments in human T cells too, given the ease of e.g., the small molecule inhibitor experiment.

The suggestions to check PIM inhibitor effects in human T cell is a good one. We think an ideal experiment would be to use naïve cord blood derived CD4 and CD8 cells as a model to avoid the impact of variability in adult PBMC and to really look at what PIM kinases do as T cells first respond to antigen and cytokines. In this context there is good evidence that the signalling pathways used by antigen receptors or the cytokines IL-2 and IL-15 are not substantially different in mouse and human. We have also previously compared proteomes of mouse and human IL-2 expanded cytotoxic T cells and they are remarkably similar. As such we feel that mature mouse CD8 T cells are a genetically tractable model to use to probe the signalling pathways that control cytotoxic T cell function. To repeat the full set of experiments observed within this study with human T cells would represent 1-year of work by an experienced postdoctoral fellow.

Unfortunately, the funding for the project has come to an end and there is no capacity to complete this work.

Would also be good for the authors to include a few experiments where PIM1/2 have been transduced back into the PIM1/2 KO T cells, to see if this reverts any differences observed in response to IL-2 - although the reviewer notes that the timeline for altering primary T cells via lentivirus/CRISPR may be on the cusp of being practical such that functional experiments can be performed on day 6 after first stimulating T cells.

A rescue experiment could indeed be informative, though of course comes with challenges/caveats with re-expressing both proteins that have been deleted at once and ability to control the level of PIM kinase that is re-expressed. This work using the Pim dKO mice was performed from 2019-2021 and was seriously impacted by the work restrictions during the COVID19 pandemic. We had to curtail all mouse colonies to allow animal staff to work within the legal guidelines. We had to make choices and the Pim1/2 dKO colony was stopped because we felt we had generated very useful data from the work but could not justify continued maintenance of the colony at such a difficult time. As such we no longer have this mouse line to perform these rescue experiments.

We have however, performed a limited number of retroviral overexpression studies in WT IL-2-expanded CTL, where T cells were transfected after 24 hours activation and phenotype measured on day 6 of culture. We chose to leave these out of the initial manuscript as these were overexpression under conditions where PIM expression was already high, rather than a true test of the ability of PIM1 or PIM2 to rescue the Pim dKO phenotype. A more robust test would also have required doing these overexpression experiments in IL-15 expanded or cytokine deprived CTL where PIM kinase expression is low, however, we ran out of time and funding to complete this work.

We have provided Author response image 1 below from the experiments performed in the IL-2 CTL for interested readers. The limited experiments that were performed do support some key phenotypes observed with the Pim dKO mice or PIM inhibitors, finding that PIM1 or PIM2 overexpression was sufficient to increase S6 phosphorylation, and provided a small further increase in GzmB expression above the already very high levels in IL-2 expanded CTL.

Author response image 1.

PIM1 or PIM2 overexpression drives increased GzmB expression and S6 phosphorylation in WT IL-2 CTL. OT1 lymph node cell suspensions were activated for 24 hours with SIINFEKL peptide (10 ng/mL), IL-2 (20 ng/mL) and IL-12 (2 ng/mL) then transfected with retroviruses to drive expression of PIM1-GFP, PIM2-GFP fusion proteins or a GFP only control. T cells were split into fresh media and IL-2 daily and (A) GzmB expression and (B) S6 phosphorylation assessed by flow cytometry in GFP+ve vs GFP-ve CD8 T cells 5 days post-transfection (i.e. day 6 of culture). Histograms are representative of 2 independent experiments.

Other experiments could also look at how PIM1/2 KO influences the differentiation of T cell populations/states during ex vivo stimulation of PBMCs or in vivo infection models using (high-dimensional) flow cytometry (rather than using bulk proteomics/RNA seq which only provide an overview of all cells combined).

We did consider the idea of in vivo experiments with the Pim1/2 dKO mice but rejected this idea as the mice have lost PIM kinases in all tissues and so we would not be able to understand if any phenotype was CD8 T cell selective. To note the Pim1/2 dKO mice are smaller than normal wild type mice (discussed further below) and clearly have complex phenotypes. An ideal experiment would be to make mice with floxed Pim1 and Pim2 alleles so that one could use cre recombinase to make a T cell-specific deletion and then study the impact of this in in vivo models. We did not have the budget or ethical approval to make these mice. Moreover, this study was carried out during the COVID pandemic when all animal experiments in the UK were severely restricted. So our objective was to get a molecular understanding of the consequences of losing theses kinases for CD8 T cells focusing on using controlled in vitro systems. We felt that this would generate important data that would guide any subsequent experiments by other groups interested in these enzymes.

We do accept the comment about bulk population proteomics. Unfortunately, single cell proteomics is still not an option at this point in time. High resolution multidimensional flow cytometry is a valuable technique but is limited to looking at only a few proteins for which good antibodies exist compared to the data one gets with high resolution proteomics.

Alongside this, performing a PCA of bulk RNA seq/proteomes or Untreated vs. IL-2 vs. IL-15 of WT and PIM1/2 knockout T cells would help cement their argument in the discussion about PIM1/2 knockout cells being distinct from a memory phenotype.

We thank the reviewer for this very good suggestion. We have now included PCAs for the RNAseq and proteomics datasets of IL-2 and IL-15 expanded WT vs Pim dKO CTL in Fig S5 and added the following text to the discussion section of the manuscript (lines 429-431):

“… and PCA plots of IL-15 and IL-2 proteomics and RNAseq data show that Pim dKO IL-2 expanded CTL are still much more similar to IL-2 expanded WT CTL than to IL-15 expanded CTL (Fig S5)”.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In panel B of Figure S1, are the smaller numbers of splenocytes found in dKO fully accounted for by a reduction in the numbers of T cells or also correspond to a reduction in B cell numbers? Are the thymus and lymph nodes showing the same trend?

We’re happy to clarify on this.

Since we were focused on T cell phenotypes in the paper this is what we have plotted in this figure, however there is also a reduction in total number of B, NK and NKT cells in the Pim dKO mice (see James et al, Nat Commun, 2021 for additional subset percentages). We find that all immune subsets we have measured make up the same % of the spleen in Pim dKO vs WT mice (we show this for T cell subsets in what was formerly Fig S1C and is now Fig S1A), the total splenocyte count is just lower in the Pim dKO mice (which we show in what was formerly Fig S1B and is now Fig S1C). To note, the Pim dKO mice were smaller than their WT counterparts (though we have not formally weighed and quantified this) and we think this is likely the major factor leading to lower total splenocyte numbers.

We have not checked the thymus so can’t comment on this. We can confirm that lymph nodes from Pim dKO mice had the same number and % CD4 and CD8 T cells as in WT.

For our in vitro studies we have made sure to either use co-cultures or for single WT and Pim dKO cultures to equalise starting cell densities between wells to account for the difference in total splenocyte number. We have now clarified this point in the methods section lines 682-684

“For generation of memory-like or effector cytotoxic T lymphocytes (CTL) from mice with polyclonal T cell repertoires, LN or spleen single cell suspensions at an equal density for WT and Pim dKO cultures (~1-3 million live cells/mL)….”

Reviewer #2 (Recommendations For The Authors):

Line 89-99 - PIM kinase expression is elevated in T cells in autoimmunity and inhibiting therefore may make some sense if PIM is enhancing T cell activity. Why then would you use an inhibitor in cancer settings? This needs better clarification for readers, with reference to T cells, particularly given this is an important justification for looking at PIM kinases in T cells.

We thank the reviewer for highlighting the lack of clarity in our explanation here.

PIM kinase inhibitors alone are proposed as anti-tumour therapies for select cancers to block tumour growth. However so far these monotherapies haven’t been very effective in clinical trials and combination treatment options with a number of strategies are being explored. There are two lines of logic for why PIM kinase inhibitors might be a good combination with an e.g. anti-PD1 or adoptive T cell immunotherapy. 1) PIM kinase inhibition has been shown to reduce inhibitory/suppressive surface proteins (e.g. PDL1) and cytokine (e.g. TGFbeta) expression in tumour cells and macrophages in the tumour microenvironment. 2) Inhibiting glycolysis and increasing memory/stem-like phenotype has been identified as desirable for longer-lasting more potent anti-tumour T cell immunity. PIM kinase inhibition has been shown to reduce glycolytic function and increase several ‘stemness’ promoting transcription factors e.g. TCF7 in a previous study. Controlled murine cancer models have shown improvement in clearance with the combination of pan-Pim kinase inhibitors and anti-PD1/PDL1 treatments (Xin et al, Cancer Immunol Res, 2021 and Chatterjee et al, Clin Cancer Res 2019).

It is worth noting, this is seemingly contradictory with other studies of Pim kinases in T cells that have generally found Pim1/2/3 deletion or inhibition in T cells to be suppressive of their function.

We have clarified this reasoning/seeming conflict of results in the introductory text as follows (lines 90-101):

“PIM kinase inhibitors have also entered clinical trials to treat some cancers (e.g. multiple myeloma, acute myeloid leukaemia, prostate cancer), and although they have not been effective as a monotherapy, there is interest in combining these with immunotherapies. This is due to studies showing PIM inhibition reducing expression of inhibitory molecules (e.g. PD-L1) on tumour cells and macrophages in the tumour microenvironment and a reported increase of stem-like properties in PIM-deficient T cells which could potentially drive longer lasting anti-cancer responses (Chatterjee et al., 2019; Xin et al., 2021; Clements and Warfel, 2022). However, PIM kinase inhibition has also generally been shown to be inhibitory for T cell activation, proliferation and effector activities (Fox et al., 2003; Mikkers et al., 2004; Jackson et al., 2021) and use of PIM kinase inhibitors could have the side effect of diminishing the anti-tumour T cell response.”  

Line 93 - The use of 'some cancers' is rather vague and unscientific - please correct phrasing like this. The same goes for lines 54 and 77 (some kinases and some analyses).

We have clarified the sentence in what is now Line 91 to include examples of some of the cancers that PIM kinase inhibitors have been explored for (see text correction in response to previous reviewer comment), which are predominantly haematological malignancies. The use of the phrase ‘some kinases’ and ‘some analyses’ in what are now Lines 52 and 75 is in our view appropriate as the subsequent sentence/(s) provide specific details on the kinases and analyses that are being referred to.

Lines 146-147 - Could it be that rather than redundancies, PIM KO is simply not influential on TCR/CD28 signalling in general but influences other pathways in the T cell?

We agree that the lack of PIM1/2 effect could also be because PIM targets downstream of TCR/CD28 are not influential and have clarified the text as follows (lines 156-161):

“These experiments quantified expression of >7000 proteins but found no substantial quantitative or qualitative differences in protein content or proteome composition in activated WT versus Pim dKO CD4 and CD8 T cells (Fig 1G-H) (Table S1). Collectively these results indicate that PIM kinases do not play an important unique role in the signalling pathways used by the TCR and CD28 to control T cell activation.”

Line 169 - Instead of specifying control - maybe put upregulate or downregulate for clarity.

We have changed the text as per reviewer suggestion (see line 183)

Line 182-183 - I would move the call out for Figure 2D to after the last call out for Figure 2C to make it more coherent for readers.

We have changed the text as per reviewer suggestion (see lines 197-200)

Line 190 - 14,000 RNA? total, unique? mRNA?

These are predominantly mRNA since a polyA enrichment was performed as part of the standard TruSeq stranded mRNA sample preparation process, however, a small number of lncRNA etc were also detected in our RNA sequencing. We left the results in as part of the overall analysis since it may be of interest to others but don’t look into it further. We do mention the existence of the non-mRNA briefly in the subsequent sentence when discussing the total number of DE RNA that were classified as protein coding vs non-coding.

We have edited this sentence as follows to more accurately reflect that the RNA being referred to is polyA+ (lines 205-207):

“The RNAseq analysis quantified ~14,000 unique polyA+ mRNA and using a cut off of >1.5 fold-change and q-value <0.05 we saw that the abundance of 381 polyA+ RNA was modified by Pim1/Pim2-deficiency (Fig 2E) (Table S2A).

Questions/points regarding figures:

Figure 1 - Is PIM3 changed in expression with the knockout of PIM1/2 in mice? Although the RNA is low could there be some compensation here? The authors put a good amount of effort in to showing that mouse T cells do not exhibit differences from knocking out pim1/2 i.e., Efforts have been made to address this using activation markers and cell size, cytokines, and proliferation and proteomics of activated T cells. What do the resting T cells look like though? Although TCR signalling is not impacted, other pathways might be. Resting-state comparison may identify this.

In all experiments Pim3 mRNA was only detected at very low levels and no PIM3 protein was detected by mass spectrometry in either wild type or PIM1/2 double KO TCR activated or cytokine expanded CD8 T cells (See Tables S1, S3, S4). There was similarly no change in Pim3 mRNA expression in RNAseq of IL-2 or IL-15 expanded CD8 T cells (See Tables S2, S6). While we have not confirmed this in resting state cells for all the conditions examined, there is no evidence that PIM3 compensates for PIM1/2deficiency or that PIM3 is substantially expressed in T cells.

Figure 1A&B - Does PIM kinase stay elevated when removing TCR stimulus? During egress from lymph node and trafficking to infection/tumour/autoimmune site, T cells experience a period of 'rest' from T-cell activation so is PIM upregulation stabilized, or does it just coincide with activation? This could be a crucial control given the rest of the study focuses on day 6 after initial activation (which includes 4 days of 'rest' from TCR stimulation). Nice resolution on early time course though.

This is an interesting question. Unfortunately, we do not know how sensitive PIM kinases are to TCR stimulus withdrawal, as we have not tried removing the TCR stimulus during early activation and measuring PIM expression.

Based on the data in Fig 2A there is a hint that 4 hours withdrawal of peptide stimulus may be enough to lose PIM1/2 expression (after ~36 hrs of TCR activation), however, we did not include a control condition where peptide is retained within the culture. Therefore, we cannot resolve this question from the current experimental data, as this difference could also be due to a further increase in PIMs in the cytokine treated conditions rather than a reduction in expression in the no cytokine condition. This ~36-hour time point is also at a stage where T cells have become more dependent on cytokines for their sustained signalling compared to TCR stimulus.

It is worth noting that PIM kinases are thought to have fairly short mRNA and protein half lives (~5-20 min for PIM1 in primary cells, ~10 min – 1 hr for PIM2). This is consistent with previous observations that cytotoxic T cells need sustained IL-2/Jak signalling to sustain PIM kinase expression, e.g. in Rollings et al (2018) Sci Signaling, DOI:10.1126/scisignal.aap8112 . We would therefore expect that sustained signalling from some external signalling receptor whether this is TCR, costimulatory receptors or cytokines is required to drive Pim1/2 mRNA and protein expression.

Figure 1D - the CD4 WT and Pim dKO plots are identical - presumably a copying error - please correct.

We apologise for the copying error and have amended the manuscript to show the correct data. We thank the reviewer for noticing this mistake.

In Figure 1H - there is one protein found significant - would be nice to mention what this is - for example, if this is a protein that influences TCR levels this could be quite important.

The protein is Phosphoribosyl Pyrophosphate synthase 1 like 1 (Prps1l1).

This was a low confidence quantification (based on only 2 peptides) with no known function in T cells. Based on what is known, this gene is predominantly expressed in the testis (though also detected in spleen, lung, liver). A whole-body KO mouse found no difference in male fertility. No further phenotype has been reported in this mouse. See: Wang et al (2018) Mol Reprod Dev, DOI: 10.1002/mrd.23053

We have added the following text to the legend of Figure 1H to address this protein:

“Phosphoribosyl Pyrophosphate synthase 1 like 1 (Prps1l1), was found to be higher in Pim dKO CD8 T cells, but was a low confidence quantification (based on only 2 unique peptides) with no known function in T cells.”

Figure S1 - In your mouse model the reduction in CD4 T cells is quite dramatic in the spleen - is this reduced homing or reduced production of T cells through development?

Could you quantify the percentage of CD45+ cells that are T cells from blood too? Would be good to have a more thorough analysis of this new mouse model.

We apologise for the lack of clarity around the Pim dKO mouse phenotype. Something we didn’t mention previously due to a lack of a formal measurement is that the Pim dKO mice were typically smaller than their WT counterparts. This is likely the main reason for total splenocytes being lower in the Pim dKO mice - every organ is smaller. It is not a phenotype reported in Pim1/2 dKO mice on an FVB background, though has been reported in the Pim1/2/3 triple KO mouse before (see Mikkers et al, Mol Cell Biol 2004 doi: 10.1128/MCB.24.13.6104-6115.2004).

The % cell type composition of the spleen is equivalent between WT and Pim dKO mice and as mentioned above, was controlled for when setting up of our in vitro cultures.

We have revised the main text and changed the order of the panels in Fig S1 to make this caveat clearer as follows (lines 138-144):

“There were normal proportions of peripheral T cells in spleens of Pim dKO mice (Fig S1A) similar to what has been reported previously in Pim dKO mice on an FVB/N genetic background (Mikkers et al., 2004), though the total number of T cells and splenocytes was lower than in age/sex matched wild-type (WT) mouse spleens (Fig S1B-C). This was not attributable to any one cell type (Fig S1A)(James et al., 2021) but was instead likely the result of these mice being smaller in size, a phenotype that has previously been reported in Pim1/2/3 triple KO mice (Mikkers et al., 2004).”

Figure S1C - why are only 10-15% of the cells alive? Please refer to this experiment in the main text if you are going to include it in the supplementary figure.

With regards what was previously Fig S1C (now Fig S1A) we apologise for our confusing labelling. We were quoting these numbers as the percentage of live splenocytes (i.e. % of live cells). Typically ~80-90% of the total splenocytes were alive by the time we had processed, stained and analysed them by flow cytometry direct ex vivo. Of these CD4 and CD8 T cells made up ~%10-15 of the total live splenocytes (with most of the rest of the live cells being B cells).  

We have modified the axis to say “% of splenocytes” to make it clearer that this is what we are plotting.

Figure S1 - Would be good to show that the T cells are truly deficient in PIM1/2 in your mice to be absolutely sure. You could just make a supplementary plot from your mass spec data.

This is a good suggestion and we have now included this data as supplementary figure 2.

To note, due to the Pim1 knockout mouse design this is not as simple as showing presence or absence of total PIM1 protein detection in this instance.

To elaborate: the Pim1/Pim2 whole body KO mice used in this study were originally made by Prof Anton Berns’ lab (Pim1 KO = Laird et al Nucleic Acids Res, 1993, doi: 10.1093/nar/21.20.4750, with more detail on deletion construct in te Riele, H. et al, Nature,1990, DOI: 10.1038/348649a0; Pim2 KO = Mikkers et al, Mol Cell Biol, 2004, DOI: 10.1128/MCB.24.13.6104-6115.2004). They were given to Prof Victor Tybulewicz on an FVB/N background. He then backcrossed them onto the C57BL/6 background for > 10 generations then gave them to us to intercross into Pim1/2 dKO mice on a C57BL/6 background.

The strategy for Pim1 deletion was as follows:

A neomycin cassette was recombined into the Pim1 gene in exon 4 deleting 296 Pim1 nucleotides. More specifically, the 98th pim-1 codon (counted from the ATG start site = the translational starting point for the 34 kDa isoform of PIM1) was fused in frame by two extra codons (Ser, Leu) to the 5th neo codon (pKM109-90 was used). The 3'-end of neo included a polyadenylation signal. The cassette also contains the PyF101 enhancer (from piiMo +PyF101) to ensure expression of neo on homologous recombination in ES cells.

Collectively this means that the PIM1 polypeptide is made prior to amino acid 98 of the 34 kDa isoform but not after this point. This deletes functional kinase activity in both the 34 kDa and 44 kDa PIM1 isoforms. Ablation of PIM1 kinase function using this KO was verified via kinase activity assay in Laird et al. Nucelic Acids Res 1993.

The strategy to delete Pim2 was as follows:

“For the Pim2 targeting construct, genomic BamHI fragments encompassing Pim2 exons 1, 2, and 3 were replaced with the hygromycin resistance gene (Pgp) controlled by the human PGK promoter.” (Mikkers et al Mol Cell Biol, 2004)

The DDA mass spectrometry data collected in Fig 1 G-H and supplementary table 1 confirmed we do not detect peptides from after amino acid residue 98 in PIM1 (though we do detect peptides prior to this deletion point) and we do not detect peptides from the PIM2 protein in the Pim dKO mice. Thus confirming that no catalytically active PIM1/PIM2 proteins were made in these mice.

We have added a supplementary figure S2 showing this and the following text (Lines 155-156):

“Proteomics analysis confirmed that no catalytically active PIM1 and PIM2 protein were made in Pim dKO mice (Fig S2).”

Figure 2A - I found the multiple arrows a little confusing - would just use arrows to indicate predicted MW of protein and stars to indicate non-specific. Why are there 3 bands/arrows for PIM2?  

The arrows have now been removed. We now mention the PIM1 and PIM2 isoform sizes in the figure legend and have left the ladder markings on the blots to give an indication of protein sizes. There are 2 isoforms for PIM1 (34 and 44 kDa) in addition to the nonspecific band and 3 isoforms of PIM2 (40, 37, 34 kDa, though two of these isoform bands are fairly faint in this instance). These are all created via ribosome use of different translational start sites from a single Pim1 or Pim2 mRNA transcript.

The following text has been added to the legend of Fig 2A:

“Western blots of PIM1 (two isoforms of 44 and 34 kDa, non-specific band indicated by *), PIM2 (three isoforms of 40, 37 and 34 kDa) or pSTAT5 Y694 expression.”

Figure 2A - why are the bands so faint for PIM1/2 (almost non-existent for PIM2 under no cytokine stim) here yet the protein expression seems abundant in Figure 1B upon stim without cytokines? Is this a sensitivity issue with WB vs proteomics? My apologies if I have missed something in the methods but please explain this discrepancy if not.

There is differing sensitivity of western blotting versus proteomics, but this is not the reason for the discrepancy between the data in Fig 1B versus 2A. These differences reflect that Fig1 B and Fig 2A contrast PIM levels in two different sets of conditions and that while proteomics allows for an estimate of ‘absolute abundance’ Western blotting only shows relative expression between the conditions assessed.  

To expand on this… Fig 1B proteomics looks at naïve versus 24 hr aCD3/aCD28 TCR activated T cells. The western blot data in Fig 2A looks at T cells activated for 1.5 days with SIINFEKL peptide and then washed free of the media containing the TCR stimulus and cultured with no stimulus for 4 or 24 hrs hours and contrast this with cells cultured with IL-2 or IL-15 for 4 or 24 hours. All Fig 2A can tell us is that cytokine stimuli increases and/or sustains PIM1 and PIM2 protein above the level seen in TCR activated cells which have not been cultured with cytokine for a given time period. Overexposure of the blot does reveal detectable PIM1 and PIM2 protein in the no cytokine condition after 4 hrs. Whether this is equivalent to the PIM level in the 24 hr TCR activated cells in Fig 1B is not resolvable from this experiment as we have not included a sample from a naïve or 24 hr TCR activated T cell to act as a point of reference.

Figure 4F - Your proteomics data shows substantial downregulation in proteomics data for granzymes and ifny- possibly from normalization to maximise the differences in the graph - and yet your flow suggests there are only modest differences. Can you explain why a discrepancy in proteomics and flow data - perhaps presenting in a more representative manner (e.g., protein counts)?

The heatmaps are a scaled for ‘row max’ to ‘row min’ copy number comparison on a linear scale and do indeed visually maximise differences in expression between conditions. This feature of these heatmaps is also what makes the lack of difference in GzmB and GzmA at the mRNA heatmap in Fig 5C quite notable.

We have now included bar graphs of Granzymes A and B and IFNg protein copy number in Figure 4 (see new Fig 4G-H) to make clearer the magnitude of the effect on the major effector proteins involved in CTL killing function. It is worth noting that flow cytometry histograms from what was formerly Fig 4G (now Fig 4I) are on a log-scale so the shift in fluorescence does generally correspond well with the ~1.7-2.75-fold reduction in protein expression observed.

Figure 4G - did you use isotype controls for this flow experiment? Would help convince labelling has worked - particularly for low levels of IFNy production.

We did not use isotype controls in these experiments but we are using a well validated interferon gamma antibody and very carefully colour panel/compensation controls to minimise background staining. The only ways to be 100% confident that an antibody is selective is to use an interferon gamma null T cell which we do not have. We do however know that the antibody we use gives flow cytometry data consistent with other orthogonal approaches to measure interferon gamma e.g. ELISA and mass spectrometry.

Figure 5M - why perform this with just the PIM kinase inhibitors? Can you do this readout for the WT vs. PIM1/2KO cells too? This would really support your claims for the paper about PIM influencing translation given the off-target effects of SMIs.

Regrettably we have not done this particular experiment with the Pim dKO T cells. As mentioned above, due to this work being performed predominantly during the COVID19 pandemic we ultimately had to make the difficult decision to cease colony maintenance. When work restrictions were lifted we could not ethically or economically justify resurrecting a mouse colony for what was effectively one experiment, which is why we chose to test this key biological question with small molecule inhibitors instead.

We appreciate that SMIs have off target effects and this is why we used multiple panPIM kinase inhibitors for our SMI validation experiments. While the use of 2 different inhibitors still doesn’t completely negate the concern about possible off-target effects, our conclusions re: PIM kinases and impact on proteins synthesis are not solely based on the inhibitor work but also based on the decreased protein content of the PIM1/2 dKO T cells in the IL-2 CTL, and the data quantifying reductions in levels of many proteins but not their coding mRNA in PIM1/2dKO T cells compared to controls.

Author Response

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

We thank the reviewers for their positive and constructive evaluations. Based upon the reviewers’ helpful comments, we have performed complementary experiments. In particular, we additionally show that:

• a complete analysis of CXCR1/2 binding chemokines in the secretions of tissular CD8+ T cells reinforces the key role of CXCL8 in CD8+ T cell-induced fibrocyte chemotaxis (new panel D in Figure 2)

• a direct contact between fibrocytes and CD8+ T cells triggers CD8+ T cell cytotoxicity against primary basal bronchial epithelial cells (new Figure 6)

• the interaction between CD8+ T cells and fibrocytes is bidirectional, with CD8+ T cells triggering the development of fibrocyte immune properties (new Figure 7)

• the characteristic time to reach a stationary state reminiscent of a resolution of the COPD condition was estimated to be about 2.5 years using the simulations. Interfering with chemotaxis and adhesion processes by inhibiting CXCR1/2 and CD54, respectively was not sufficient to reverse the COPD condition, as predicted by the mathematical model (new Figure 9)

• the massive proliferation effect induced by fibrocytes is specific to CD8+ T cells and not CD4+ T cells (new Figure 3-figure supplement 2), and that fibrocytes moderately promote the death of unactivated CD8+ T cells in direct co-culture (new Figure 3-figure supplement 3)

We have graphically summarized our findings (new Figure 10) suggesting the existence of a positive feedback loop playing a role in the vicious cycle that promotes COPD. A new table describing patient characteristics for basal bronchial epithelial cell purification has also been added (new Supplementary File 9), the Supplementary Files 7 and S8 have been up-dated to take into account the new experiments.

The mass spectrometry proteomics data have been deposited to the ProteomeXchange Consortium (http://proteomecentral.proteomexchange.org) via the PRIDE partner repository with the dataset identifier PXD041402.  

Reviewer #1 (Recommendations For The Authors):

The experimental approaches are all rationally designed and the data clearly presented, with appropriate analyses and sample sizes. I could find no technical or interpretative concerns. The interrelationship between the observational data (histology) with the quantitative live cell imaging and the follow-on functional investigations is especially laudable. The data nicely unifies several years of accumulated data regarding the (separate) participation of CD8 T cells and fibrocytes in COPD.

We thank the reviewer for his/her comments.

I have only minor comments:

1) Line 79: The observation that T cells may influence fibrocyte differentiation/function was initially made some years earlier by Abe et al (J Immunol 2001; 7556), and should be cited in addition to the follow-on work of Niedermeyer.

This reference has been added to acknowledge this seminal work.

2) Line 632: Corticosteroids originate from the cortex of the adrenal gland. Budenoside and fluticasone are glucocorticoids, not corticosteroids.

This mistake has been corrected in the discussion of the revised manuscript (see line 802 in the revised manuscript).

3) Given the state of T cell immunotherapies, cytokine/chemokine antagonists, and emerging fibrocyte-targeted drugs, can the authors possibly speculate as to desired pathways to target therapeutically?

Chemokine-receptor based therapies could be used to inhibit fibrocyte recruitment into the lungs, such as CXCR4 blockade. We have very recently shown that using the CXCR4 antagonist, plerixafor, alleviates bronchial obstruction and reduces peri-bronchial fibrocytes density (Dupin et al., 2023). Because CXCR4 expression in human fibrocytes is dependent on mTOR signaling and is inhibited by rapamycin in vitro (Mehrad et al., 2009), alternative strategies consisting of targeting fibrocytes via mTOR have been proposed. This target has proven effective in bronchiolitis obliterans, idiopathic pulmonary fibrosis, and thyroid-associated ophthalmopathy, using rapamycin (Gillen et al., 2013; Mehrad et al., 2009), sirolimus (Manjarres et al., 2023) or an insulin-like growth factor-1 (IGF-I) receptor blocking antibody (Douglas et al., 2020; Smith et al., 2017). Inhibiting mTOR is also expected to have effects on CD8+ T cells, ranging from an immunostimulatory effect by activation of memory CD8+ T-cell formation, to an immunosuppressive effect by inhibition of T cell proliferation (Araki et al., 2010). Last, chemokine-receptor base therapies could also include strategies to inhibit the CD8+-induced fibrocyte chemotaxis, such as dual CXCR1-CXCR2 blockade. We were able to test this latter strategy in our mathematical model, see response to point 6 of reviewer 2.

Immunotherapies directly targeting the interaction between fibrocytes and CD8+ T cells could also be considered, such as CD86 or CD54 blockade. The use of abatacept and belatacept, that interfere with T cell co-stimulation, is effective in patients with rheumatoid arthritis (Pombo-Suarez & Gomez-Reino, 2019) and in kidney-transplant recipients (Vincenti et al., 2016), respectively. Targeting the IGF-I receptor by teprotumumab in the context of thyroid-associated ophthalmopathy also improved disease outcomes, possibly by altering fibrocyte-T cell interactions (Bucala, 2022; Fernando et al., 2021).

We also tested this CD86 and CD54 blocking strategy for COPD treatment by simulations, see response to point 6 of reviewer 2.

However, such therapies should be used with caution as they may favour adverse events such as infections, particularly in the COPD population (Rozelle & Genovese, 2007). Additionally, the fibrocytes-lymphocytes interaction has recently been shown to promote anti-tumoral immunity via the PD1-PDL1 immunological synapse (Afroj et al., 2021; Mitsuhashi et al., 2023). Therefore, care should be taken in the selection of patients to be treated and/or timing of treatment administration with regards to the increased risk of lung cancer in COPD patients.

The discussion section has been altered accordingly.

4) The authors may want to consider mentioning (and citing) recent insight into the immune-mediated fibrosis in thyroid-associated ophthalmopathy

These important publications are now cited in a dedicated paragraph about the possible therapeutical interventions (see answer to point 3, and discussion in the revised manuscript).

Reviewer #2 (Recommendations For The Authors):

Specific comments

1) The rationale for the selection of chemokines overexpressed by CD8+ T cells in COPD is based on literature data of n=2 patients per group. This is limited and risky. I am less concerned about false positives given the selection of chemokines and the available literature but am worried about the possibility that many chemokines may not have been selected based on insufficient power to do meaningful stats on this comparison. For example, many other CXCR1/2 binding CXCL chemokines exist and these could contribute to the migration effect in Fig 2C as well. Given the currently available single-cell resources it should be possible to extend these observations and to investigate CXCL chemokine expression in COPD CD8 T cells to the benefit of Fig 2A in full detail.

We agree with the reviewer that the rationale for the selection of chemokines of interest could be reinforced by the analysis of supplementary single-cell resources. We used data from the COPD cell atlas (Gene Expression Omnibus GSE136831 (Sauler et al., 2022)) to perform such an analysis of chemokine expression by CD8+ CD103+ and CD8+ CD103- T cells. However, the expression level of all chemokines was globally very low, and was not different between control and COPD patients (see Author response image 1).

Author response image 1.

Expression of CXC chemokines in lung CD8+ CD103+ and CD8+ CD103- T cells from patients with COPD (n=18 independent samples) in comparison with healthy control subjects (n=29 independent samples) under resting conditions by Single-Cell RNA sequencing analysis (GEO accession GSE136831). The heatmaps show the normalized expression of genes (horizontal axes) encoding CXC chemokines. PF4=CXCL4, PPBP= CXCL7.

The latter results are in discrepancy with those resulting from transcriptomic analysis of microarray data obtained on purified lung CD8+ CD103+ and CD8+ CD103- T cells, showing a significant level of chemokines expression (Hombrink et al., 2016), and a differential expression of CCL2, CCL26, CXCL2, CXCL8 and CCL3L1 between CD8+ T lymphocytes of control and COPD patients (Figure 2A in the revised manuscript). The reason for these differences is unclear, and could be attributed to biological differences (samples obtained from different patients) or, more likely, to differences in sample processing (cell sorting by flow cytometry for microarray analysis, that could activate minimally CD8+ cells) and/or methodological differences (differences of sensitivity between microarray and scRNA seq).

Nevertheless, microarray data regarding CXCL8 expression are in good agreement with our in vitro experiments, showing an enhanced CXCL8 expression by CD8+ T cells purified from COPD lungs, in comparison with that of control subjects. In addition, the CXCL8 blocking antibody fully abrogates the increase of migration induced by secretion of COPD CD8+ T cells, to the same extent as the blocking of CXCR1/2 by reparixin. This suggests that this supplementary chemotaxis is mainly due to CXCL8 and not other CXCR1/2 binding CXCL chemokines, and correlates CXCL8 measurements to functional experiments. This precision has been now added in the results section of the revised version.

2) Equally, it would strengthen the work if multiplex ELISA assays could be provided on the supernatants used in Fig 2D to provide a more comprehensive view of CXCR1/2 binding chemokines.

In order to have a complete view of CXCR1/2 binding chemokines, we have now performed supplementary ELISA assays to measure the concentrations of CXCL1, 3, 5, 6 and 7, in addition of the measurements of CXCL2 and CXCL8 already presented in the previous version of the manuscript (Figure 2D). Results of these new assays are now presented in the revised version of Figure 2. Concentrations of CXCL1, 3, 5, 6 and 7 were unchanged between the control and COPD conditions.

3) In the functional analyses, I missed information on the activation of the fibrocytes. Equally, the focus on CD8 T cells was mainly on proliferation in the functional work. RNAseq analyses on the cells, comparing CD8 T cells and fibrocytes, alone and in co-culture to each other would help to identify interaction patterns in comprehensive detail. Such an experiment would bolster the significance of the studies by providing impact analysis not only on the T cells beyond proliferation but by expanding on the effect of the interaction on the fibrocyte as well.

Regarding the activation state of fibrocytes, we apologize if this was not clear: in our in vitro co-culture experiments, we chose not to activate the fibrocytes. This setting is in agreement with previous findings, demonstrating an antigen-independent T cell proliferation effect driven by fibrocytes (Nemzek et al., 2013), and it is now explicitly written in the results of the revised manuscript.

Regarding the focus of the functional analyses:

First, we have pushed forward the analysis of the consequences of the interaction beyond CD8+ T cells proliferation. In particular, having shown that fibrocytes promote CD8+ T cells expression of cytotoxic molecules such as granzyme B, we decided to investigate the cytotoxic capacity of CD8+ T cells against primary basal bronchial epithelial cells (see new Supplementary File 9 in the revised manuscript for patient characteristics).

Direct co-culture with fibrocytes increased total and membrane expression of the cytotoxic degranulation marker CD107a, which was only significant in non-activated CD8+ T cells (see new Figure 6A-E in the revised manuscript). A parallel increase of cytotoxicity against primary epithelial cells was observed in the same condition (see new Figure 6F-H in the revised manuscript). This demonstrates that following direct interaction with fibrocytes, CD8+ T cells have the ability to kill target cells such as bronchial epithelial cells. This is now included in the results section of the revised manuscript.

Second, we have now performed proteomic analyses on fibrocytes, alone or in co-culture during 6 days with CD8+ T cells either non-activated or activated (see new Figure 7A in the revised manuscript). Of the top ten pathways that were most significantly activated in co-cultured vs mono-cultured fibrocytes, largest upregulated genes were those of the dendritic cell maturation box, the multiple sclerosis signaling pathway, the neuroinflammation signaling pathway and the macrophage classical signaling pathway, irrespective of the activation state of CD8+ T cells (see new Figure 7B in the revised manuscript). The changes were globally identical in the two conditions of CD8+ T cell activation, with some upregulation more pronounced in the activated condition. They were mostly driven by up-regulation of a core set of Major Histocompatibility Complex class I (HLA-B, C, F) and II (HLA-DMB, DPA1, DPB1, DRA, DRB1, DRB3) molecules, co-simulatory and adhesion molecules (CD40, CD86 and CD54). Another notable proteomic signature was that of increased expression of IFN signaling-mediators IKBE and STAT1, and the IFN-responsive genes GBP2, GBP4 and RNF213. We also observed a strong downregulation of CD14, suggesting fibrocyte differentiation, and an upregulation of the matrix metalloproteinase-9 (MMP9) in the non-activated condition only. Altogether, these changes suggest that the interaction between CD8+ T cells and fibrocytes promotes the development of fibrocyte immune properties, which could subsequently impact the activation of CD4+ T cells activation.

Up-regulated pathways identified in proteomic profile of fibrocytes co-cultured with CD8+ T cells are very consistent with a shift towards a proinflammatory phenotype rather than towards a reparative role. The activation of IFN-γ signaling could be triggered by CD8+ T cell secretion of IFN upon fibrocyte interaction, suggesting the existence of a positive feedback loop (see new Figure 10). Additionally, the priming of fibrocytes by CD8+ T cells could also induce CD4+ T cell activation.

4) I suggest rewording the abstract to capture the main storyline and wording more. The abstract is good, but I see so many novelties in the paper that are not well sold in the abstract, particularly the modelling aspects.

As suggested by the reviewer, we revised the abstract, as shown below and in the revised manuscript. The changes are indicated in red:

Revised abstract:

Bronchi of chronic obstructive pulmonary disease (COPD) are the site of extensive cell infiltration, allowing persistent contacts between resident cells and immune cells. Tissue fibrocytes interaction with CD8+ T cells and its consequences were investigated using a combination of in situ, in vitro experiments and mathematical modeling. We show that fibrocytes and CD8+ T cells are found in vicinity in distal airways and that potential interactions are more frequent in tissues from COPD patients compared to those of control subjects. Increased proximity and clusterization between CD8+ T cells and fibrocytes are associated with altered lung function. Tissular CD8+ T cells from COPD patients promote fibrocyte chemotaxis via the CXCL8-CXCR1/2 axis. Live imaging shows that CD8+ T cells establish short-term interactions with fibrocytes, that trigger CD8+ T cell proliferation in a CD54- and CD86-dependent manner, pro-inflammatory cytokines production, CD8+ T cell cytotoxic activity against bronchial epithelial cells and fibrocyte immunomodulatory properties. We defined a computational model describing these intercellular interactions and calibrated the parameters based on our experimental measurements. We show the model’s ability to reproduce histological ex vivo characteristics, and observe an important contribution of fibrocyte-mediated CD8+ T cell proliferation in COPD development. Using the model to test therapeutic scenarios, we predict a recovery time of several years, and the failure of targeting chemotaxis or interacting processes. Altogether, our study reveals that local interactions between fibrocytes and CD8+ T cells could jeopardize the balance between protective immunity and chronic inflammation in bronchi of COPD patients.

5) The probabilistic model appears to suggest that reduced CD8 T cell death may also explain the increase in the pathology in COPD. Did the authors find that fibrocytes reduce cell death of the CD8 T cells?

Taking advantage of the staining of CD8+ T cells with the death marker Zombie NIR™, we have quantified CD8+ T cell death in our co-culture assay. The presence of fibrocytes in the indirect co-culture assay did not affect CD8+ T cell death (see new Figure 3-figure supplement 3A-B in the revised manuscript). In direct co-culture, the death of CD8+ T cells was significantly increased in the non-activated condition but not in the activated condition (see new Figure 3-figure supplement 3C-D in the revised manuscript). Of note, these results are in agreement with a recent study showing the existence of CD8+ T cell-population-intrinsic mechanisms regulating cellular behavior, with induction of apoptosis to avoid an excessive increase in T cell population (Zenke et al., 2020). This is taken into account in our mathematical model by an increased probability p_(dC+) of dying when a CD8+ T cell is surrounded by many other T cells in its neighborhood. It also suggests that the reduced CD8+ T cell death evidenced in tissues from patients with COPD (Siena et al., 2011) might not be due to the specific interplay between fibrocyte and CD8+ T cells, but rather to a global pro-survival environment in COPD lungs.

These new data have been described in the results section.

6) Following the modeling in Figure 6, curiosity came to mind, which is how long it would take for the pathology to disappear if a drug would be applied to the patient. How much should the interactions be reduced and how long would it take to reach clinical benefit? Could such predictions be made? I understand that this may be outside the main message of the manuscript but perhaps this could be included in the discussion.

This is a very interesting question, that we have addressed by performing additional simulations to investigate the outcomes of possible therapeutic interventions. First, we applied a COPD dynamics during 20 years, to generate the COPD state, that provide the basis for treatment implementation. Then, we applied a COPD dynamic during 7 years, that mimics the placebo condition (see new Figure 9A in the revised manuscript, and below), that we compared to a control dynamics (“Total inhibition”), that mimics an ideal treatment able to restore all cellular processes. As expected the populations of fibrocytes and CD8+ T cells, as well as the density of mixed clusters, decreased. These numbers reached levels similar of healthy subjects after approximately 2.5 years, and this time point can therefore be considered as the steady state (Figure 9B-E).

Monitoring of the different processes revealed that these effects were mainly due to a reduction in fibrocyte-induced CD8+ T duplication, and a transient or more prolonged increase in basal fibrocyte and CD8+ T death (Figure 9C-D).

Then, three possible realistic treatments were considered (Figure 9A). We tested the effect of directly inhibiting the interaction between fibrocytes and CD8+ T cells by blocking CD54. This was implemented in the model by altering the increased probability of a CD8+ T cell to divide when a fibrocyte is in its neighbourhood, as shown by the co-culture results (Figure 4). We also chose to reflect the effect of a dual CXCR1/2 inhibition by setting the displacement function of fibrocyte similar to that of control dynamics, in agreement with the in vitro experiments (Figure 2E). Blocking CD54 only slightly reduced the density of CD8+ T cells compared to the placebo condition, and had no effect on fibrocyte and mixed cluster densities (Figure 9B). CXCR1/2 inhibition was a little bit more potent on the reduction of CD8+ T cells than CD54 inhibition, and it also significantly decreased the density of mixed clusters (Figure 9B). As expected, this occurred through a reduction of fibrocyte-induced duplication, which was affected more strongly by CXCR1/2 blockage than by CD54 blockage (Figure 9C-E). Combining both therapies (CD54 and CXCR1/2 inhibition) did not strongly major the effects (Figure 9B-E). In all the conditions tested, the size of the fibrocyte population remained unchanged, suggesting that other processes such as fibrocyte death or infiltration should be targeted to expect broader effects.

The results section has been altered accordingly.

Using the simulations, we were also able to estimate the characteristic time to reach a stationary state reminiscent of a resolution of the COPD condition. This time of approximately 2.5 years was totally unpredictable by in vitro experiments, and indicates that a treatment aiming at restoring these cellular processes should be continued during several years to obtain significant changes.

We have also investigated the outcomes of more realistic treatments, modifying specifically processes such as chemotaxis or targeting directly the intercellular interactions. The modification of parameters controlling these processes only slightly affected the final state, suggesting that such treatments may be more effective when used in combination with other drugs e.g. those affecting fibrocyte infiltration and/or death.

The discussion section has been altered accordingly.

Reviewer #3 (Recommendations For The Authors):

1) Broader assessment of cell types in the lung: Staining for other cell types such as dendritic cells, CD4 cells, and interstitial macrophages, and comparing their proximity to fibrocytes with that of CD8 cells would better justify the CD8 focus.

We agree with the reviewer that multiple stainings would have better justified the focus on CD8+ T cells. However, it is difficult to distinguish fibrocytes, dendritic cells and interstitial macrophages on the basis of immunohistochemistry, as we and others previously showed (Dupin et al., 2019; Mitsuhashi et al., 2015; Pilling et al., 2009). On the other hand, the study of Afroj et al. indicated the possible interaction between fibrocytes and CD8+ T cells in cancer context, with the induction of CD8+ T cell proliferation (Afroj et al., 2021). This T cell-costimulatory function of fibrocytes and CD8+ T cells was further confirmed in a very recent study, together with the antitumor effects of PD-L1 and VEGF blockade (Mitsuhashi et al., 2023). These data, along with the specific implication on CD8+ T cells in COPD, relying mainly on their abundance in COPD bronchi (O’Shaughnessy et al., 1997), their overactivation state (Roos-Engstrand et al., 2009), their cytotoxic phenotype (Freeman et al., 2010; Wang et al., 2020) and the protection against lung inflammation and emphysema induced by their depletion (Maeno et al., 2007) justified the CD8 focus.

To further justify this focus, we have now performed co-culture between fibrocytes and CD4+ T cells, indicating that the massive fibrocyte-mediated proliferation was specific to CD8+ T cells (see answer to comment 3 below). This is in agreement with the results obtained with the simulations, showing that considering fibrocytes and CD8+ T cells only was sufficient to reproduce the spatial patterns in the bronchi of healthy and COPD patients. Altogether, we think that focusing on the CD8+ T cell-fibrocyte interplay was pertinent in the context of COPD. It does obviously not exclude the possibility of other interactions, that could be the focus of other studies.

2) Transcriptomic analysis: Using n=2 and only showing the chemokines as well as selected adhesion receptor data narrows the focus but does not provide broader insights into the interactions. Using a more robust sample size and performing a comprehensive pathway analysis would represent an unbiased analysis to determine the most dysregulated pathways. Importantly, the authors could use a single-cell RNA-seq dataset to broadly assess the transcriptomes of several cell types in the lung (such as the data from (Sauler et al, Characterization of the COPD alveolar niche using single-cell RNA sequencing).

This very pertinent suggestion has also been raised by reviewer 2, see our answer to comment 1 of reviewer 2, and below:

We agree with the reviewer that the rationale for the selection of chemokines of interest could be reinforced by the analysis of supplementary single-cell resources. We used data from the COPD cell atlas (Gene Expression Omnibus GSE136831 (Sauler et al., 2022)) to perform such an analysis of chemokine expression by CD8+ CD103+ and CD8+ CD103- T cells. However, the expression level of all chemokines was globally very low, and was not different between control and COPD patients (see Figure scRNAseq, in the answer to comment 1 of reviewer 2).

These latter results are in discrepancy with those resulting from transcriptomic analysis of microarray data obtained on purified lung CD8+ CD103+ and CD8+ CD103- T cells, showing a significant level of chemokines expression (Hombrink et al., 2016), and a differential expression of CCL2, CCL26, CXCL2, CXCL8 and CCL3L1 between CD8+ T lymphocytes of control and COPD patients (Figure 2A in the revised manuscript). The reason for these differences is unclear, and could be attributed to biological differences (samples obtained from different patients) or, more likely, to differences in sample processing (cell sorting by flow cytometry for microarray analysis, that could activate minimally CD8+ cells) and/or methodological differences (differences of sensitivity between microarray and scRNA seq).

Nevertheless, microarray data regarding CXCL8 expression are in good agreement with our in vitro experiments, showing an enhanced CXCL8 expression by CD8+ T cells purified from COPD lungs, in comparison with that of control subjects. In addition, the CXCL8 blocking antibody fully abrogates the increase of migration induced by secretion of COPD CD8+ T cells, to the same extent as the blocking of CXCR1/2 by reparixin. This suggests that this supplementary chemotaxis is mainly due to CXCL8 and not other CXCR1/2 binding CXCL chemokines, and correlates CXCL8 measurements to functional experiments. This precision has been now added in the text of the revised version.

3) Inclusion of control/comparison cell types in co-culture studies would help establish that CD8 cells are more relevant for interactions with fibrocytes than for example CD4 cells.

We have now performed co-cultures between fibrocytes and CD4+ T cells, with the same settings than for CD8+ T cells. The results from these experiments show that fibrocytes did not have any significant effect of CD4+ T cells death, regardless of their activation state (see new Figure 3-figure supplement 2A-C in the revised manuscript, and below). Fibrocytes were able to promote CD4+ T cells proliferation in the activated condition but not in the non-activated condition (see new Figure 3-figure supplement 2A-D in the revised manuscript). Altogether this indicates that although fibrocyte-mediated effect on proliferation is not specific to CD8+ T cells, the amplitude of the effect is much larger on CD8+ T cells than on CD4+ T cells.

These new data have been added in the results section.

4) In vitro analysis of cells from non-COPD patients would also help assess whether the circulating cells from COPD patients have a level of baseline activation which promotes the vicious cycle but may not exist in healthy cells.

Regarding circulating cells, the present study relies on the COBRA cohort (COhort of BRonchial obstruction and Asthma), which includes only asthma and COPD patients, and therefore does not grant access to healthy subjects’ blood samples (Pretolani et al., 2017). Unfortunately, we have no other ongoing study with healthy subjects that would allow us to retrieve blood for research, and fibrocytes can only be grown from freshly drawn blood samples. We agree with the reviewer that it is a limitation of our study, which is now acknowledged at the end of the discussion section.  

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This important study investigated the role of oxytocin (OT) neurons in the paraventricular nucleus (PVN) and their projections to the medial prefrontal cortex (mPFC) in regulating pup care and infanticide behaviors in mandarin voles. The researchers used techniques like immunofluorescence, optogenetics, OT sensors, and peripheral OT administration. Activating OT neurons in the PVN reduced the time it took pup-caring male voles to approach and retrieve pups, facilitating pup-care behavior. However, this activation had no effect on females. Interestingly, this same PVN OT neuron activation also reduced the time for both male and female infanticidal voles to approach and attack pups, suggesting PVN OT neuron activity can promote pup care while inhibiting infanticide behavior. Inhibition of these neurons promoted infanticide. Stimulating PVN->mPFC OT projections facilitated pup care in males and in infanticide-prone voles, activation of these terminals prolonged latency to approach and attack. Inhibition of PVN->mPFC OT projections promoted infanticide. Peripheral OT administration increased pup care in males and reduced infanticide in both sexes. However, some results differed in females, suggesting other mechanisms may regulate female pup care.

Strengths:

This multi-faceted approach provides converging evidence, strengthens the conclusions drawn from the study, and makes them very convincing. Additionally, the study examines both pup care and infanticide behaviors, offering insights into the mechanisms underlying these contrasting behaviors. The inclusion of both male and female voles allows for the exploration of potential sex differences in the regulation of pup-directed behaviors. The peripheral OT administration experiments also provide valuable information for potential clinical applications and wildlife management strategies.

Weaknesses:

While the study presents exciting findings, there are several weaknesses that should be addressed. The sample sizes used in some experiments, such as the Fos study and optogenetic manipulations, appear to be small, which may limit the statistical power and generalizability of the results. Effect sizes are not reported, making it difficult to evaluate the practical significance of the findings. The imaging parameters and analysis details for the Fos study are not clearly described, hindering the interpretation of these results (i.e., was the entire PVN counted?). Also, does the Fos colocalization align with previous studies that look at PVN Fos and maternal/ paternal care? Additionally, the study lacks electrophysiological data to support the optogenetic findings, which could provide insights into the neural mechanisms underlying the observed behaviors. 

In some previous studies (He et al., 2019; Mei, Yan, Yin, Sullivan, & Lin, 2023), the sample size in morphological studies is also small and may be representative. We agree with reviewer’s opinion that results from larger sample size may be more statistically powerful and generalizable. We will pay attention to this issue in the future study. As reviewer suggested, we have added effect size both in the source data and in the main text, including d, η2  and odds ratio. We have added the objective magnification used in the figure legend. The imaging parameters and analysis details for the Fos study have also been added in the revised manuscript. Brain slices of 40 µm thick were collected consecutively on 4 slides, each slide had 6 brain slices spaced 160 µm apart from each other. PVN area were determined based on the Allen Mouse Brain Atlas and our previous study, and Fos, OT and merged positive neurons were counted. Our result about Fos and OT colocalization is consistent with previous study. In a previous study on virgin male prairie voles, OT and Fos colabeled neurons in the PVN increased after exposure to conspecific pups and experiencing paternal care (Kenkel et al., 2012). In another study of prairie voles, OT and c-fos colabeled neurons in PVN significantly increased after becoming parents which may be due to a shift from virgin to parents (Kelly, Hiura, Saunders, & Ophir, 2017). To support the optogenetic findings, we used c-Fos expression as a marker of neuron activity and revealed significant increases/decreases of c-Fos positive neurons induced by optogenetic activation/inhibition (Supplementary Data Fig. 1), and additionally we found that optogenetic inhibition of OT neurons reduced levels of OT release using OT1.0 sensors. Based on these two experiments, we verified that optogenetic manipulation in the present study is validate and results of optogenetic experiment are reliable (Supplementary Data Fig. 5).

The study has several limitations that warrant further discussion. Firstly, the potential effects of manipulating OT neurons on the release of other neurotransmitters (or the influence of other neurochemicals or brain regions) on pup-directed behaviors, especially in females, are not fully explored. Additionally, it is unclear whether back-propagation of action potentials during optogenetic manipulations causes the same behavioral effect as direct stimulation of PVN OT cells. Moreover, the authors do not address whether the observed changes in behavior could be explained by overall increases or decreases in locomotor activity.

We agree with reviewer’s suggestion that several limitations should be discussed. Although we used a virus strategy to specifically activate or inhibit PVN OT neurons, other neurochemical may also be released during optogenetic manipulations because OT neurons may also release other neurochemicals. In one of our previous studies, activation of the OT neuron projections from the PVN to the VTA as well as to the Nac brain also altered pup-directed behaviors, which may also be accompanied by dopamine release (He et al., 2021). In addition, backpropagation of action potentials during optogenetic manipulations may also causes the same behavioral effect as direct stimulation of PVN OT cells. These effects on pup-directed behaviors should also be investigated further in the future study. For the optogenetics experiments, we have referred to some of the previous research (Mei et al., 2023; Murugan et al., 2017), and in our study we have also carried out the verification of the reliability of the methods. To exclude effects of locomotor activity on pup directed behaviors, we also investigated effect of optogenetic manipulations on the locomotor activity of experimental animals and found that optogenetic manipulation did not change levels of locomotor activity (Supplementary Data Fig. 6).

The authors do not specify the percentage of PVN->mPFC neurons labeled that were OT-positive, nor do they directly compare the sexes in their behavioral analysis (or if they did, it is not clear statistically). While the authors propose that the sex difference in pup-directed behaviors is due to females having greater OT expression, they do not provide evidence to support this claim from their labeling data. It is also uncertain whether more OT neurons were manipulated in females compared to males. The study could benefit from a more comprehensive discussion of other factors that could influence the neural circuit under investigation, especially in females.

AAV11-Ef1a-EGFP virus can infect fibers and retrogradely reach to cell body, thus this virus can be used to retrogradely trace neurons. We injected this virus (green, AAV11-Ef1a-EGFP) in the mPFC and observed virus infected and OT (red) positive neuron in the PVN (Yellow), and we also counted the OT neurons that project from PVN to mPFC and found that approximately 45.16% and 40.79% of cells projecting from PVN to the mPFC were OT-positive, and approximately 18.48% and 18.89% of OT cells in the PVN projected to the mPFC in females and males, respectively (Supplementary Data Fig. 4). In addition, as reviewers suggested, we compared the numbers of OT neurons, activated OT neurons (OT and Fos double-labeled neurons) and level of OT release between males and females. We found that females have more activated OT neurons (Figure1, d, g) and released higher levels of OT into the mPFC (Figure 4 d, e) than males. This part has been added in the result and discussion. We did not analyze whether more OT neurons were manipulated in females compared to males, which is indeed a limitation of this study that requires our attention. 

As the reviewers suggested, we also discussed other factors that could influence the neural circuit under investigation. In addition to OT neurons, OTR neurons may also regulate behavioral responses to pups. In a study of virgin female mice, pup exposure was found to activate oxytocin and oxytocin receptor expressing neurons (Okabe et al., 2017). Other brain regions such as preoptic area (POA) may also be involved in parental behaviors. For example, virgin female mice repeatedly exposed to pups showed shorter retrieval latencies and greater c-Fos expression in the preoptic area (POA), concentrations of OT in the POA were also significantly increased, and the facilitation of alloparental behavior by repeated exposure to pups occurred through the organization of the OT system (Okabe et al., 2017). A recent study suggests that OT of the PVN is involved in the care of pups by male voles (He et al., 2021). This study suggests that PVN to ventral tegumental area (VTA) OT projections as well as VTA to nucleus accumbens (NAc) DA projections are involved in the care of pups by male voles. Inhibition of OT projections from the PVN to the VTA reduces DA release in the NAc during licking and grooming of pups (He et al., 2021). The effects of these factors on pup-directed responses should also be considered in the future study. 

Reviewer #2 (Public Review):

Summary:

This series of experiments studied the involvement of PVN OT neurons and their projection to the mPFC in pup-care and attack behavior in virgin male and female Mandarin voles. Using Fos visualization, optogenetics, fiber photometry, and IP injection of OT the results converge on OT regulating caregiving and attacks on pups. Some sex differences were found in the effects of the manipulations.

Strengths:

Major strengths are the modern multi-method approaches and involving both sexes of Mandarin vole in every experiment.

Weaknesses:

Weaknesses include the lack of some specific details in the methods that would help readers interpret the results. These include:

(1) No description of diffusion of centrally injected agents.

Thanks for your professional consideration. Individuals with appropriate viral expression and optical fiber implant location were included in the statistical analysis, otherwise excluded. For optogenetic experiments, the virus (AAV2/9-mOXT-hCHR2(H134R)–mCherry-ER2-WPRE-pA or rAAV-mOXT-eNpHR3.0-mCherry-WPRE-hGH-pA) was designed and constructed to only infect OT neurons, which limited the diffusion of the virus. For fiber photometric experiments, the OT1.0 sensor was largely able to restrict expression within the mPFC brain region, and additionally individuals with incorrect optical fiber embedding position were not included in the statistical analysis. The diffusion of central optogenetic viruses and OT1.0 sensors are shown in the supplemental figure (Supplementary Data Fig. 7).

(2) Whether all central targets were consistent across animals included in the data analyses. This includes that is not stated if the medial prelimbic mPFC target was in all optogenetic study animals as shown in Figure 4 and if that is the case, there is no discussion of that subregion's function compared to other mPFC subregions.

As shown in Figure 4 and in the schematic diagram of the optogenetic experiment, the central targets of virus infection and fiber location remain consistent in the data analysis, otherwise the data would be excluded. In the present study, viruses were injected into the prelimbic (PrL). The PrL and infralimbic (IL) regions of the mPFC play different roles in different social interaction contexts (Bravo-Rivera, Roman-Ortiz, Brignoni-Perez, Sotres-Bayon, & Quirk, 2014; Moscarello & LeDoux, 2013). A study has shown that the PrL region of the mPFC contributes to active avoidance in situations where conflict needs to be mitigated, but also contributes to the retention of conflict responses for reward (Capuzzo & Floresco, 2020). This may reveal that the suppression of infanticide by PVN to mPFC OT projections is a behavioral consequence of active conflict avoidance. In a study on pain in rats, OT neurons projections from the PVN to the PrL were found to increase the responsiveness of cell populations in the PrL, suggesting that OT may act by altering the local excitation-inhibition (E/I) balance in the PrL (Liu et al., 2023). A study on anxiety-related behaviors in male rats suggests that the anxiolytic effects of OT in the mPFC are PrL-specific but not infralimbic or anterior cingulate and that this is achieved primarily through the engagement of GABAergic neurons, which ultimately modulate downstream anxiety-related brain regions, including the amygdala (Sabihi, Dong, Maurer, Post, & Leuner, 2017). This finding may provide possible downstream pathways for further research. 

(3) How groups of pup-care and infanticidal animals were created since there was no obvious pretest mentioned so perhaps there was the testing of a large number of animals until getting enough subjects in each group.  

Before the experiments, we exposed the animals to pups, and subjects may exhibit pup care, infanticide, or neglect; we grouped subjects according to their behavioral responses to pups, and individuals who neglected pups were excluded.

(4) The apparent use of a 20-minute baseline data collection period for photometry that started right after the animals were stressed from handling and placement in the novel testing chamber.

In fiber photometric experiments, all experimental animals were required to acclimatize to the environment for at least 20 minutes prior to the experiment as described in the Methods section. The time 0 in Fig. 4 represents the point in time when a behavior or a segment of behavior started and is not the actual time 0 at which the test was started.

(5) A weakness in the results reporting is that it's unclear what statistics are reported (2 x 2 ANOVA main effect of interaction results, t-test results) and that the degrees of freedom expected for the 2 X 2 ANOVAs in some cases don't appear to match the numbers of subjects shown in the graphs; including sample sizes in each group would be helpful because the graph panels are very small and data points overlap.

Thanks for your suggestion. We displayed analysis methods for the data statistics and the sample sizes for each group of experiments in the figure legends.

The additional context that could help readers of this study is that the authors overlook some important mPFC and pup caregiving and infanticide studies in the introduction which would help put this work in better context in terms of what is known about the mPFC and these behaviors. These previous studies include Febo et al., 2010; Febo 2012; Peirera and Morrell, 2011 and 2020; and a very relevant study by Alsina-Llanes and Olazábal, 2021 on mPFC lesions and infanticide in virgin male and female mice. The introduction states that nothing is known about the mPFC and infanticide. In the introduction and discussion, stating the species and sex of the animals tested in all the previous studies mentioned would be useful. The authors also discuss PVN OT cell stimulation findings seen in other rodents, so the work seems less conceptually novel. Overall, the findings add to the knowledge about OT regulation of pup-directed behavior in male and female rodents, especially the PVN-mPFC OT projection.

We appreciate you very much to provide so many valuable references. We have cited them in the introduction and discussion. We agree with the reviewer’s opinion that nothing is known about the mPFC and infanticide is incorrect. It should be whether mPFC OT projections are involved in paternal cares and infanticide remains unclear. A study in mother rats indicated that inactivation or inhibition of neuronal activity in the mPFC largely reduced pup retrieval and grouping (Febo, Felix-Ortiz, & Johnson, 2010). In a subsequent study on firing patterns in the mPFC of mother rats suggested that sensory-motor processing occurs in the mPFC that may affect decision making of maternal care to their pups (Febo, 2012). In a study on new mother rats examining different regions of the mPFC (anterior cingulate (Cg1), PrL, IL), they identified a involvement of the IL cortex in biased preference decision-making in favour of the offspring (Pereira & Morrell, 2020). A study on maternal motivation in rats suggests that in the early postpartum period, the IL and Cg1 subregion in mPFC, are the motivating circuits for pup-specific biases (Pereira & Morrell, 2011), while the PrL subregion, are recruited and contribute to the expression of maternal behaviors in the late postpartum period (Pereira & Morrell, 2011).

Reviewer #3 (Public Review):

Summary:

Here Li et al. examine pup-directed behavior in virgin Mandarin voles. Some males and females tend towards infanticide, others tend towards pup care. c-Fos staining showed more oxytocin cells activated in the paraventricular nucleus (PVN) of the hypothalamus in animals expressing pup care behaviors than in infanticidal animals. Optogenetic stimulation of PVN oxytocin neurons (with an oxytocin-specific virus to express the opsin transgene) increased pup-care, or in infanticidal voles increased latency towards approach and attack.

Suppressing the activity of PVN oxytocin neurons promoted infanticide. The use of a recent oxytocin GRAB sensor (OT1.0) showed changes in medial prefrontal cortex (mPFC) signals as measured with photometry in both sexes. Activating mPFC oxytocin projections increased latency to approach and attack in infanticidal females and males (similar to the effects of peripheral oxytocin injections), whereas in pup-caring animals only males showed a decrease in approach. Inhibiting these projections increased infanticidal behaviors in both females and males and had no effect on pup caretaking.

Strengths:

Adopting these methods for Mandarin voles is an impressive accomplishment, especially the valuable data provided by the oxytocin GRAB sensor. This is a major achievement and helps promote systems neuroscience in voles.

Weaknesses:

The study would be strengthened by an initial figure summarizing the behavioral phenotypes of voles expressing pup care vs infanticide: the percentages and behavioral scores of individual male and female nulliparous animals for the behaviors examined here. Do the authors have data about the housing or life history/experiences of these animals? How bimodal and robust are these behavioral tendencies in the population?

As our response to reviewer 2, animals generally exhibit three types of behavioral responses toward pups, and data on the percentage of these different behavioral types occurring in the group will be included in another study in our lab. The reviewer's suggestion of scoring the behaviors is an inspiring idea that will help us to more fully parse these behaviors. Mandarin voles were captured from the wild in Henan, China. The experimental subjects were F2 generation voles reared in the Experimental Animal Centre of Shaanxi Normal University. In our observations, pup care and infanticide behaviors were conserved across several pup exposures, especially pup care behaviors, whereas for infanticide behaviors we did not conduct more pup exposures in order to protect the pups. 

Optogenetics with the oxytocin promoter virus is a nice advance here. More details about their preparation and methods should be in the main text, and not simply relegated to the methods section. For optogenetic stimulation in Figure 2, how were the stimulation parameters chosen? There is a worry that oxytocin neurons can co-release other factors- are the authors sure that oxytocin is being released by optogenetic stimulation as opposed to other transmitters or peptides, and acting through the oxytocin receptor (as opposed to a vasopressin receptor)?

As reviewer suggested, more detailed information about virus construction and choice of optogenetic stimulation parameter have been added in the revised manuscript. The details about the construction of CHR2 and mCherry viruses used in optogenetic manipulation can refer to a previous study in which they constructed an rAAV-expressing Venus from a 2.6 kb region upstream of OT exon 1, which is conserved in mammalian species (Knobloch et al., 2012). For details about construction of the eNpHR 3.0 virus, expression of the vector is driven by the mouse OXT promoter, a 1kb promoter upstream of exon 1 of the OXT gene, which has been shown to induce cell type-specific expression in OXT cells (Peñagarikano et al., 2015). Details about the construction of OT1.0 sensor can be referred to the research of Professor Li's group (Qian et al., 2023). The mapping of the viral vectors and OT1.0 sensor is shown below. 

The optogenetic stimulation parameters were used based on a previous study (He et al., 2021). However, our description of the parameters in the experiment is still not in detail, so some information about optogenetic stimulation parameters has been added in the method. In pupdirected pup care behavioral test, light stimulation lasted for 11 min. Parameters used in optogenetic manipulation of PVN OT neurons were ~ 3 mW, 20 Hz, 20 ms, 8 s ON and 2 s OFF and parameters used in optogenetic manipulation of PVN OT neurons projecting to mPFC were ~ 10 mW, 20 Hz, 20 ms, 8 s ON and 2 s OFF to cover the entire interaction. We performed fiber photometric experiments to determine the role that OT plays in behavior, and these results were able to support each other with optogenetic experiments. In addition, we further confirmed the role of optogenetic manipulation on OT release in combination with optogenetic inhibition and OT1.0 sensors (Supplementary Data Fig. 2). It has been previously shown that OT is able to act specifically on OTR in mPFC-PL (Sabihi et al., 2017). Our study focuses on oxytocin neurons as well as oxytocin release, and more research is needed to construct a more complex and complete network regarding the involvement of the OTR and other factors in the mPFC in these behaviors.

Author response image 1.

Author response image 2.

Given that they are studying changes in latency to approach/attack, having some controls for motion when oxytocin neurons are activated or suppressed might be nice. Oxytocin is reported to be an anxiolytic and a sedative at high levels.

As our response to reviewer 1, to exclude effects of locomotor activity on pup directed behaviors, we also investigated effect of optogenetic manipulations on the locomotor activity of experimental animals and found that optogenetic manipulation did not change levels of locomotor activity (Supplementary Data Fig. 6).

The OT1.0 sensor is also amazing, these data are quite remarkable. However, photometry is known to be susceptive to motion artifacts and I didn't see much in the methods about controls or correction for this. It's also surprising to see such dramatic, sudden, and large-scale suppression of oxytocin signaling in the mPFC in the infanticidal animals - does this mean there is a substantial tonic level of oxytocin release in the cortex under baseline conditions?

The optical fiber recording system used in the present study can automatically exclude effects of motion artifacts by simultaneously recording signals stimulated by a 405nm light source. As shown in the formula below, the z-score data were calculated and presented, and the increase and decline of the OT signal is a trend relative to the baseline. For a smooth baseline, the decreasing signal is generally amplified after calculation. In our experiments combining optogenetic inhibition and OT1.0 sensors, we were able to find that there was a certain level of OT release at baseline, on which there was room for a decrease in the signal recorded by the OT1.0 sensor.

Figure 5 is difficult to parse as-is, and relates to an important consideration for this study: how extensive is the oxytocin neuron projection from PVN to mPFC?

AAV11-Ef1a-EGFP virus can infect fiber and retrogradely reach to cell body, thus this virus can be used to retrogradely trace neurons. We injected the this virus (green, AAV11-Ef1aEGFP) in the mPFC and observed virus infected and OT (red) positive neuron in the PVN (Yellow), and we also counted the OT neurons that project from PVN to mPFC and found that approximately 45.16% and 40.79% of cells projecting from PVN to the mPFC were OT-positive, and approximately 18.48% and 18.89% of OT cells in the PVN projected to the mPFC in females and males, respectively (Supplementary Data Fig. 4).  

In Figures 6 and 7, the authors use the phrase 'projection terminals'; however, to my knowledge, there have not been terminals (i.e., presynaptic formations opposed to a target postsynaptic site) observed in oxytocin neuron projections into target central regions.

According your suggestion, we replaced the ‘terminals’ with ‘fibers’ to describe it more accurately..

Projection-based inhibition as in Figure 7 remains a controversial issue, as it is unclear if the opsin activation can be fast enough to reduce the fast axonal/terminal action potential. Do the authors have confirmation that this works, perhaps with the oxytocin GRAB OT sensor?

Thanks for your suggestion. We measured the OT release using OT1.0 sensors when the OT neuron projections in the mPFC were optogenetically inhibited. The result showed that optogenetic inhibition of OT neuron fibers in the mPFC significantly reduced OT release that validate the method of projection-based inhibition (Supplementary Data Fig. 5).

As females and males had similar GRAB OT1.0 responses in mPFC, why would the behavioral effects of increasing activity be different between the sexes?

In the present study, females released higher levels of OT into the mPFC (Figure 4 d, e) than males upon occurrence of different behaviors. In addition, females already exhibited more rapid approach and retrieval of pups than male before the optogenetic activation this may be the reason no effects of this manipulation were found in female.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Check for spelling and grammar errors throughout.

Thanks to the reviewer's suggestion, we have checked and revised the article.

(2) Report effect sizes for all significant findings to allow evaluation of practical significance.

As reviewer suggested, we have added effect size both in the source data and in the main text, including d, η2  and odds ratio.

(3) Provide detailed information on the imaging parameters and analysis methods used in the Fos study.

The imaging parameters and analysis details for the Fos study have also been added in the revised manuscript. Brain slices of 40 µm thick were collected consecutively on 4 slides, each slide had 6 brain slices spaced 160 µm apart from each other. PVN area were determined based on the Allen Mouse Brain Atlas and our previous study, andFos, OT and merged positive neurons were counted.

(4) Compare the Fos colocalization results with previous studies examining PVN Fos and maternal/paternal care to contextualize the findings.

Our result about Fos and OT colocalization is consistent with previous study. In a previous study on virgin male prairie voles, OT and Fos colabeled neurons in the PVN increased after exposure to conspecific pups and experiencing paternal care (Kenkel et al., 2012). In another study of prairie voles, OT and c-fos colabeled neurons in PVN significantly increased after becoming parents which may be due to a shift from virgin to parents (Kelly et al., 2017).

(5) Discuss the limitations of the study, such as the potential effects of manipulating OT neurons on the release of other transmitters or the influence of other neurochemicals or brain regions on pupdirected behaviors, especially in females.

We agree with reviewer’s suggestion that several limitations should be discussed. Although we used a virus strategy to specifically activate or inhibit PVN OT neurons, other neurochemical may also be released during optogenetic manipulations because OT neurons may also release other neurochemicals. In one of our previous studies, activation of the OT neuron projections from the PVN to the VTA as well as to the Nac brain also altered pup-directed behaviors, which may also be accompanied by dopamine release (He et al., 2021). In addition, backpropagation of action potentials during optogenetic manipulations may also causes the same behavioral effect as direct stimulation of PVN OT cells. These effects on pup-directed behaviors should also be investigated further in the future study.

(6) Address the possibility of back-propagation of action potentials in the optogenetic manipulations causing the same behavioral effects as PVN OT cell stimulation.

We agree with the reviewer’s opinion hat optogenetic manipulation may possibly induce back-propagation of action potentials that may result in same behavioral effects as OT cell stimulation. We will pay attention to this issue in the future study.  

(7) Investigate whether changes in locomotor behavior could explain the observed effects on pupdirected behaviors.

To exclude effects of locomotor activity on pup directed behaviors, we also investigated effect of optogenetic manipulations on the locomotor activity of experimental animals and found that optogenetic manipulation did not change levels of locomotor activity (Supplementary Data Fig. 6).

(8) Report the percentage of PVN->mPFC neurons labeled that were OT-positive.

AAV11-Ef1a-EGFP virus can infect fiber and retrogradely reach to cell body, thus this virus can be used to retrogradely trace neurons. We injected this virus (green, AAV11-Ef1a-EGFP) in the mPFC and observed virus infected and OT (red) positive neuron in the PVN (Yellow), and we also counted the OT neurons that project from PVN to mPFC and found that approximately 45.16% and 40.79% of cells projecting from PVN to the mPFC were OT-positive, and approximately 18.48% and 18.89% of OT cells in the PVN projected to the mPFC in females and males, respectively (Supplementary Data Fig. 4).

(9)  Directly compare the sexes in the behavioral analysis and discuss any potential sex differences.

We agree with the reviewer's suggestion and have added comparisons between two sexes and discussion about relevant results. 

(10) If available, report and discuss the OT expression levels and the number of OT neurons manipulated in each sex.

In the present study, we have counted the number of OT cells, but did not measure the level of OT expression using WB or qPCR. In addition, the percentages of CHR2(H134R) and eNpHR3.0 virus infected neurons in total OT positive neurons were presented (Supplementary Data Fig. 7), but we did not know how many cells were actually manipulated during the optogenetic experiment.

(11) Expand the discussion to include what could be regulating or interacting with the OT circuit under investigation, particularly in females where the effects were less pronounced.

As the reviewers suggested, we have also added relevant discussion. In addition to OT neurons, OTR neurons may also regulate behavioral responses to pups. In a study of virgin female mice pup exposure was found to activate oxytocin and oxytocin receptor expressing neurons (Okabe et al., 2017). Other brain regions such as preoptic area (POA) may also be involved in parental behaviors. For example, virgin female mice repeatedly exposed to pups showed shorter retrieval latencies and greater c-Fos expression in the preoptic area (POA), concentrations of OT in the POA were also significantly increased, and the facilitation of alloparental behavior by repeated exposure to pups occurred through the organization of the OT system (Okabe et al., 2017). A recent study suggests that OT of the PVN is involved in the care of pups by male voles (He et al., 2021). This study suggests that PVN to ventral tegumental area (VTA) OT projections as well as VTA to nucleus accumbens (NAc) DA projections are involved in the care of pups by male voles. Inhibition of OT projections from the PVN to the VTA reduces DA release in the NAc during licking and grooming of pups (He et al., 2021).

Reviewer #2 (Recommendations For The Authors):

A few additional things the authors may want to consider:

(1) I don't understand the subject numbers in the peripheral OT study data shown in Figure 8. Panels p and q have 69 females shown and 50 males. Was there a second, much larger, IP injection study conducted that was different than the subjects shown in panels a-o that had ~5 subjects per treatment group per sex?

Sorry for the confusing. More animals were used to test effects of OT on infanticide behaviors in our pre-test. These data combined with data from formal pharmacological experiment were presented in Fig. 8p, q. After OT treatment, the changes in detailed and specific behaviors were only collected in several animals. We have clarified that in the revised manuscript. 

(2) The authors suggest higher baseline OT release in the female mPFC, which makes sense and helps explain some of their results. It seems that the data in Figure 1 show what is probably no sex difference in OT cell numbers in the PVN of Mandarin voles, which is unlike the old studies in mice or rats. If readers look at the data in Figure 1 showing what seems to be no sex difference in OT cell number, the authors' argument in the discussion about mPFC OT release levels higher in females would be inconsistent with their own data shown. The authors have the brain sections they need to help support or undermine this argument in the discussion, so maybe it would be useful to analyze the OT cell numbers across the PVN and report it in this paper or briefly mention it in the discussion.

We compared the numbers of OT neurons, activated OT neurons (OT and Fos doublelabeled neurons) and level of OT release between males and females. We found that females have more activated OT neurons (Figure1, d, g) and released higher levels of OT into the mPFC (Figure 4 d, e) than males. This part has been added in the result and discussion. The inconsistency of the OT cell numbers with previous studies may be due to the method of cell counting, as we did not count all slides consecutively.  

(3) The discussion suggests visual cues are involved in mPFC OT release relevant for pup care or infanticide, but this is a very odd claim for nocturnal animals that live and nest with their pups in underground burrows.

Sorry for the confusing. Here, we cited the finding in mice that activation of PVN OT neurons induced by visual stimulation promoted pup care to support our finding that the activity of OT cells of the PVN is involved in pup care, rather than to illustrate the role of visual stimulation in voles. We have clarified that in the revised manuscript.

(4) The lack of decrease in mPFC OT release in the 2nd and 3rd approaches to pups is probably because the release was so high after the 1st approach that it didn't have time to drop before the subsequent approaches. The authors don't state how long those between-approach intervals were on average to help readers interpret this result.

As described in our methods, we spaced about 60 s between each behavioral test to allow the signal return back to the baseline level.

(5) Do PVN-mPFC OT somata collateralize to other brain sites? Could mPFC terminal stimulation activate entire PVN cells and every site they project to? A caveat could be mentioned in the discussion if there's support for this from other optogenetic and PVN OT cell projection studies.

We verified the OT projections from PVN to mPFC, to validate the optogenetic manipulation of this pathway, but did not investigate whether the OT neurons projecting from PVN to mPFC also project collaterally to other brain regions. It is suggested that mPFC terminal stimulation only activate PVN OT cells projecting mPFC, whether other OT neurons were activated remains unclear. 

(6) I don't see an ethics statement related to the experiments obviously having to involve pup injury or death. Nothing is said in methods about what happened after adult subjects attacked pups. I assumed the tests were quickly terminated and pups euthanized.

In case the pups were attacked, we removed them immediately to avoid unnecessary injuries, and injured pups were euthanized.

(7) The authors could be more specific about what psychological diseases they refer to in the abstract and elsewhere that are relevant to this study. Depression? Rare cases of psychosis? Even within the already rare parental psychosis, infanticide is tragic but rare.

Infanticide is caused by a variety of factors, mental illness, especially depression and psychosis, is often a very high risk factor among them (Milia & Noonan, 2022; Naviaux, Janne, & Gourdin, 2020). In human, infanticide has been used to refer to the killing, neglect or abuse of newborn babies and older children (Jackson, 2006). Here, we believe that research on the neural mechanisms of infanticide can also contribute to the understanding and treatment of attacks on children, physical and verbal abuse, and direct killing of babies. 

(8) Figure 8 - in one case the "*" is a chi-square result , correct?

Thanks for your careful checking. In Figure 8p, q, we applied the chi-square test and  added it in the legend.

Reviewer #3 (Recommendations For The Authors):

The only other thing is a typo on line 135: the authors mean 'stimulation' instead of 'simulation'.

Corrected.

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Author response:

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

Reviewer #1 (Public Review):  

Summary:

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

Strengths:

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

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

- Linking the multivariate activity patterns to memory behavior is critical in thinking about the potential differential roles of cortical areas in sub-serving successful working memory. Figure 3 nicely shows a similar interaction to that of Figure 2 in the role of sPCS in the categorization vs. maintenance tasks.

- The cross-decoding analysis in Figure 4 is a clever and interesting way to parse out how stimulus and rule/category information may be intertwined, which would have been one of the foremost potential questions or analyses requested by careful readers. However, I think more additional text in the Methods and Results to lay out the exact logic of this abstract category metric will help readers bet0ter interpret the potential importance of this analysis and result.

We thank the reviewer for the positive assessment of our manuscript. Please see lines 366-372, 885-894 in the revised manuscript for a detailed description of the abstract category index, and see below for a detailed point-by-point response.

Weaknesses:

- Selection and presentation of regions of interest: I appreciate the authors' care in separating the sPCS region as "frontal cortex", which is not necessarily part of the prefrontal cortex, on which many ideas of working memory maintenance activity are based. However, to help myself and readers interpret these findings, at a minimum the boundaries of each ROI should be provided as part of the main text or extended data figures. Relatedly, the authors use a probabilistic visual atlas to define ROIs in the visual, parietal, and frontal cortices. But other regions of both lateral frontal and parietal cortices show retinotopic responses (Mackey and Curtis, eLife, 2017: https://elifesciences.org/articles/22974) and are perhaps worth considering. Do the inferior PCS regions or inferior frontal sulcus show a similar pattern of effects across tasks? And what about the middle frontal gyrus areas of the prefrontal cortex, which are most analogous to the findings in NHP studies that the authors mention in their discussion, but do not show retinotopic responses? Reporting the effects (or lack thereof) in other areas of the frontal cortex will be critical for readers to interpret the role of the frontal cortex in guiding WM behavior and supporting the strongly worded conclusions of broad frontal cortex functioning in the paper. For example, to what extent can sPCS results be explained by visual retinotopic responses? (Mackey and Curtis, eLife, 2017: https://elifesciences.org/articles/22974).

We thank the reviewer for the suggestions. We have added a Supplemental Figure 1 to better illustrate the anatomical locations of ROIs.  

Following the reviewer’s suggestion, we defined three additional subregions in the frontal cortex based on the HCP atlas [1], including the inferior precentral sulcus (iPCS, generated by merging 6v, 6r, and PEF), inferior frontal sulcus (IFS, generated by merging IFJp, IFJa, IFSp, IFSa, and p47r), and middle frontal gyrus (MFG, generated by merging 9-46d, 46, a9-46v, and p9-46v). We then performed the same analyses as in the main text using both mixed-model and within-condition IEMs. Overall, we found that none of the ROIs demonstrated significant orientation representation in Experiment 1, for either IEM analysis (Author response image 1A and 1C). In Experiment 2, however, the IFS and MFG (but not iPCS) demonstrated a similar pattern to sPCS for orientation representation, though these results did not persist in the within-condition IEM with lower SNR (Author response image 1B and 1D). Moreover, when we performed the abstract category decoding analysis in the three ROIs, only the MFG in Experiment 2 showed significant abstract category decoding results, with no significant difference between experiments (Author response image 1E). To summarize, the orientation and category results observed in sPCS in the original manuscript were largely absent in other frontal regions. There was some indication that the MFG might share some results for orientation representation and category decoding, although this pattern was weaker and was only observed in some analyses in Experiment 2. Therefore, although we did not perform retinotopic mapping and cannot obtain a direct measure of retinotopic responses in the frontal cortex, these results suggest that our findings are unlikely to be explained by visual retinotopic responses: the iPCS, which is another retinotopic region, did not show the observed pattern in any of the analyses. Notably, the iPCS results are consistent with our previous work demonstrating that orientation information cannot be decoded from iPCS during working memory delay [2]. We have included these results on lines 395-403, 563-572 in the revised manuscript to provide a more comprehensive understanding of the current findings. 

Author response image 1.

Orientation reconstruction and abstract category decoding results in iPCS, IFS, and MFG.

- When looking at the time course of effects in Figure 2, for example, the sPCS maintenance vs categorization effects occur very late into the WM delay period. More information is needed to help separate this potential effect from that of the response period and potential premotor/motor-related influences. For example, are the timecourses shifted to account for hemodynamic lag, and if so, by how much? Do the sPCS effects blend into the response period? This is critical, too, for a task that does not use a jittered delay period, and potential response timing and planning can be conducted by participants near the end of the WM delay. For example, the authors say that " significant stimulus representation in EVC even when memoranda had been transformed into a motor format (24)". But, I *think* this paper shows the exact opposite interpretation - EVC stimulus information is only detectable when a motor response *cannot* be planned (https://elifesciences.org/articles/75688). Regardless, parsing out the timing and relationship to response planning is important, and an ROI for M1 or premotor cortex could also help as a control comparison point, as in reference (24).

We thank the reviewer for raising this point. We agree that examining the contribution of response-related activity in our study is crucial, as we detail below:

First, the time course results in the manuscript are presented without time shifting. The difference in orientation representation in Figure 2 emerged at around 7 s after task cue onset and 1 s before probe onset. Considering a 4-6 s hemodynamic response lag, the difference should occur around 1-3 s after task cue onset and 5-7 s prior to probe onset. This suggests that a substantial portion of the effect likely occurred during the delay rather than response period.

Second, our experimental design makes it unlikely that response planning would have influenced our results, as participants were unable to plan their motor responses in advance due to randomized response mapping at the probe stage on a trial-by-trial basis. Moreover, even if response planning had impacted the results in sPCS, it would have affected both conditions similarly, which again, would not explain the observed differences between conditions.

Third, following the reviewer’s suggestion, we defined an additional ROI (the primary motor cortex, M1) using the HCP atlas and repeated the IEM analysis. No significant orientation representation was observed in either condition in M1, even during the response period (Figure S3), further suggesting that our results are unlikely to be explained by motor responses or motor planning.

Based on the evidence above, we believe motor responses or planning are unlikely to account for our current findings. We have included these results on lines 264-267 to further clarify this issue.

Lastly, upon re-reading the Henderson et al. paper [3], we confirmed that stimulus information was still decodable in EVC when a motor response could be planned (Figure 2 of Henderson et al.). In fact, the authors also discussed this result in paragraph 5 of their discussion. This finding, together with our results in EVC, indicates that EVC maintains stimulus information in working memory even when the information is no longer task-relevant, the functional relevance of which warrants further investigation in future research.

- Interpreting effect sizes of IEM and decoding analysis in different ROIs. Here, the authors are interested in the interaction effects across maintenance and categorization tasks (bar plots in Figure 2), but the effect sizes in even the categorization task (y-axes) are always larger in EVC and IPS than in the sPCS region... To what extent do the authors think this representational fidelity result can or cannot be compared across regions? For example, a reader may wonder how much the sPCS representation matters for the task, perhaps, if memory access is always there in EVC and IPS? Or perhaps late sPCS representations are borrowing/accessing these earlier representations? Giving the reader some more intuition for the effect sizes of representational fidelity will be important. Even in Figure 3 for the behavior, all effects are also seen in IPS as well. More detail or context at minimum is needed about the representational fidelity metric, which is cited in ref (35) but not given in detail. These considerations are important given the claims of the frontal cortex serving such an important for flexible control, here.

We thank the reviewer for raising this point. We agree that the effect sizes are always larger in EVC and IPS. This is because the specific decoding method we adopted, IEM, is based on the concept of population-level feature-selective responses, and decoding results would be most robust in regions with strong feature-tuning responses, such as EVC and parts of IPS. Therefore, to minimize the impact of effect size on our results, we avoided direct comparisons of representational strength across ROIs, focusing instead on differences in representational strength between conditions within the same ROI. With this approach, we found that EVC and IPS showed high representational fidelity throughout the trial, but only in sPCS did we observe significant higher fidelity in categorization condition, where orientation was actually not a behavioral goal but was manipulated in working memory to achieve the goal. Moreover, although representational fidelity in the EVC was the highest, its behavioral predictability decreased during the delay period, unlike sPCS. These results suggest that the magnitude of fidelity alone is not the determining factor for the observed categorization vs. maintenance effect or for behavioral performance. We have included further discussion on this issue on lines 208-211 of the revised manuscript.

The reviewer also raised a good point that IPS showed similar behavioral correlation results as sPCS. In the original manuscript, we discussed the functional similarities and distinctions between IPS and sPCS in the discussion. We have expanded on this point on lines 610-627 in the revised manuscript:

“While many previous WM studies have focused on the functional distinction between sensory and frontoparietal cortex, it has remained less clear how frontal and parietal cortex might differ in terms of WM functions. Some studies have reported stimulus representations with similar functionality in frontal and parietal cortex [4, 5], while others have observed differential patterns [6-8]. We interpret the differential patterns as reflecting a difference in the potential origin of the corresponding cognitive functions. For example, in our study, sPCS demonstrated the most prominent effect for enhanced stimulus representation during categorization as well as the tradeoff between stimulus difference and category representation, suggesting that sPCS might serve as the source region for such effects. On the other hand, IPS did show visually similar patterns to sPCS in some analyses. For instance, stimulus representation in IPS was visually but not statistically higher in the categorization task. Additionally, stimulus representation in IPS also predicted behavioral performance in the categorization task. These results together support the view that our findings in sPCS do not occur in isolation, but rather reflect a dynamic reconfiguration of functional gradients along the cortical hierarchy from early visual to parietal and then to frontal cortex.”

Lastly, following the reviewer’s suggestion, we have included more details on the representational fidelity metric on lines 201-206, 856-863 in the revised manuscript for clarity.

Recommendations:

Figure 3 layout - this result is very interesting and compelling, but I think could be presented to have the effect demonstrated more simply for readers. The scatter plots in the second and third rows take up a lot of space, and perhaps having a barplot as in Figure 2 showing the effects of brain-behavior correlations collapsed across the WM delay period timing would make the effect stand out more.

We thank the reviewer for the suggestion. We have added a subplot (C) to Figure 3 to demonstrate the brain-behavior correlation collapsed across the late task epoch.

When discussing the link between sPCS representations and behavior, I think this paper should likely be cited ([https://www.jneurosci.org/content/24/16/3944](https://www.jneurosci.org/content/24/ 16/3944)), which shows univariate relationships between sPCS delay activity and memory-guided saccade performance.

We thank the reviewer for the suggestion and have included this citation on lines 278-279 in the revised manuscript.

Interpretation of "control" versus categorization - the authors interpret that "It would be of interest to further investigate whether this active control in the frontal cortex could be generalized to tasks that require other types of WM control such as mental rotation." I think more discussion on the relationship between categorization and "control" is needed, especially given the claim of "flexible control" throughout. Is stimulus categorization a form of cognitive control, and if so, how?  

We thank the reviewer for raising this point. Cognitive control is generally defined as the process by which behavior is flexibly adapted based on task context and goals, and most theories agree that this process occurs within working memory [9, 10]. With this definition, we consider stimulus categorization to be a form of cognitive control, because participants needed to adapt the stimulus based on the categorization rule in working memory for subsequent category judgements. With two categorization rules, the flexibility in cognitive control increased, because participants need to switch between the two rules multiple times throughout the experiment, instead of being fixed on one rule. We now clarify these two types of controls on lines 112-116 in the introduction.

However, we agree that the latter form of control could be more related to rule switching that might not be specific to categorization per se. For instance, if participants perform rule switching in another type of WM task that requires WM control such as mental rotation, it remains to be tested whether similar results would be observed and/or whether same brain regions would be recruited. We have included further information on this issue on lines 572-575 in the revised manuscript.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

We thank the reviewer for the positive assessment of our manuscript.

Weaknesses:

While the RNN model matches some of the properties of the task and decoding, its ability to reproduce the detailed findings of the paper was limited. Overall, the RRN model was not as well-motivated as the fMRI analyses.

We are grateful for the reviewer’s suggestions on improving our RNN results. Please see below for a detailed point-by-point response.

Recommendations:

Overall, I thought that this paper was excellent. I have some conceptual concerns about the RNN model, and minor recommendations for visualization.

(1) I think that the RNN modelling was certainly interesting and well-executed. However, it was not clear how much it contributed to the results. On the one hand, it wasn't clear why reproducing the stimulus was a critical objective of the task (ie could be more strongly motivated on biological grounds). On the other hand, the agreement between the model and the fMRI results is not that strong. The model does not reproduce stronger decoding in 'EVC' for maintenance vs categorization. Also, the pattern of abstract decoding is very different from the fMRI (eg the RNN has stronger categorical encoding in 'EVC' than 'PFC' and larger differences between fixed and flexible rules in earlier areas than is evident in the fMRI). Together, the RNN modelling comes across as a little ad hoc, without really nailing the performance.

We thank the reviewer for prompting us to further elaborate on the rationale for our RNN analysis. In our fMRI results, we observed a tradeoff between maintaining stimulus information in more flexible tasks (Experiment 1) and maintaining abstract category information in less flexible tasks (Experiment 2). This led to the hypothesis that participants might have employed different coding strategies in the two experiments. Specifically, in flexible environments, stimulus information might be preserved in its original identity in the higher-order cortex, potentially reducing processing demands in each task and thereby facilitating efficiency and flexibility; whereas in less flexible tasks, participants might generate more abstract category representations based on task rules to facilitate learning. To directly test this idea, we examined whether explicitly placing a demand for the RNN to preserve stimulus representation would recapitulate our fMRI findings in frontal cortex by having stimulus information as an output, in comparison to a model that did not specify such a demand. Meanwhile, we totally agree with the reviewer that there are alternative ways to implement this objective in the model. For instance, changing the network encoding weights (lazy vs. rich regime) to make feedforward neural networks either produce high-dimensional stimulus or low-dimensional category representations [11]. However, we feel that exploring these alternatives may fall outside the scope of the current study.

Regarding the alignment between the fMRI and RNN results: for the stimulus decoding results in EVC, we found that with an alternative decoding method (IEM), a similar maintenance > categorization pattern was observed in EVC-equivalent module, suggesting that our RNN was capable of reproducing EVC results, albeit in a weaker manner (please see our response to the reviewer’s next point). For the category decoding results, we would like to clarify that the category decoding results in EVC was not necessarily better than those in sPCS. Although category decoding accuracy was numerically higher in EVC, it was more variable compared to IPS and sPCS. To illustrate this point, we calculated the Bayes factor for the category decoding results of RNN2 in Figure 6C, and found that the amount of evidence for category decoding as well as for the decoding difference between RNNs in IPS and sPCS modules was high, whereas the evidence in the EVC was insufficient (Response Table 1).

Author response table 1.

Bayes factors for category decoding and decoding differences in Figure 6C lower panel.

Nevertheless, we agree with the reviewer that all three modules demonstrated the category decoding difference between experiments, which differs from our fMRI results. This discrepancy may be partially due to differences in signal sensitivity. RNN signals typically have a higher SNR compared to fMRI signals, as fMRI aggregates signals from multiple neurons and single-neuron tuning effects can be reduced. We have acknowledged this point on lines 633-636 in the revised manuscript. Nonetheless, the current RNNs effectively captured our key fMRI findings, including increased stimulus representation in frontal cortex as well as the tradeoff in category representation with varying levels of flexible control. We believe the RNN results remain valuable in this regard.

Honestly, I think the paper would have a very similar impact without the modelling results, but I appreciate that you put a lot of work into the modeling, and this is an interesting direction for future research. I have a few suggestions, but nothing that I feel too strongly about.

- It might be informative to use IEM to better understand the RNN representations (and how similar they are to fMRI). For example, this could show whether any of the modules just encode categorical information. 

- You could try providing the task and/or retro cue directly to the PFC units. This is a little unrealistic, but may encourage a stronger role for PFC.

- You might adjust the ratio of feedforward/feedback connections, if you can find good anatomical guidance on what these should be.

Obviously, I don't have much - it's a tricky problem!

We thank the reviewer for the suggestions. To better align the fMRI and RNN results, we first performed the same IEM analyses used in the fMRI analyses on the RNN data. We found that with IEM, the orientation representation in the EVC module demonstrated a pattern similar to that in the fMRI data, showing a negative trend for the difference between categorization and maintenance, although the trend did not reach statistical significance (Author response image 2A). Meanwhile, the difference between categorization and maintenance remained a positive trend in the sPCS module.

Second, following the reviewer’s suggestion, we adjusted the ratio of feedforward/feedback connections between modules to 1:2, such that between Modules 1 and 2 and between Modules 2 and 3, there were always more feedback than feedforward connections, consistent with recent theoretical proposals [12]. We found that, this change preserved the positive trend for orientation differences in the sPCS module, but in the meantime also made the orientation difference in the EVC and IPS modules more positive (Author response image 2B).

To summarize, we found that the positive difference between categorization and maintenance in the sPCS module was robust across difference RNNs and analytical approaches, further supporting that RNNs with stimulus outputs can replicate our key fMRI findings in the frontal cortex. By contrast, the negative difference between categorization and maintenance in EVC was much weaker. It was weakly present using some analytical methods (i.e., the IEM) but not others (i.e., SVMs), and increasing the feedback ratio of the entire network further weakened this difference. We believe that this could be due to that the positive difference was mainly caused by top-down, feedback modulations from higher cortex during categorization, such that increasing the feedback connection strengthens this pattern across modules. We speculate that enhancing the negative difference in the EVC module might require additional modules or inputs to strengthen fine-grained stimulus representation in EVC, a mechanism that might be of interest to future research. We have added a paragraph to the discussion on the limitations of the RNN results on lines 629-644.

Author response image 2.

Stimulus difference across RNN modules.  (A). Results using IEM (p-values from Module 1 to 3: 0.10, 0.48, 0.01). (B). Results using modified RNN2 with changed connection ratio (p-values from Module 1 to 3: 0.12, 0.22, 0.08). All p-values remain uncorrected.

(2) Can you rule out that during the categorization task, the orientation encoding in PFC isn't just category coding? You had good controls for category coding, but it would be nice to see something for orientation coding. e.g., fit your orientation encoding model after residualizing category encoding, or show that category encoding has worse CV prediction than orientation encoding.

We thank the reviewer for raising this point. To decouple orientation and category representations, we performed representational similarity analysis (RSA) in combination with linear mixed-effects modeling (LMEM) on the fMRI data. Specifically, we constructed three hypothesized representational dissimilarity matrices (RDMs), one for graded stimulus (increasing distance between orientations as they move farther apart, corresponding to graded feature tuning responses), one for abstract category (0 for all orientations within the same category and 1 for different categories), and another for discrete stimulus (indicating equidistant orientation representations). We then fit the three model RDMs together using LMEM with subject as the random effect (Author response image 3A). This approach is intended to minimize the influence of collinearity between RDMs on the results [13].

Overall, the LMEM results (Author response image 3B-D) replicated the decoding results in the main text, with significant stimulus but not category representation in sPCS in Experiment 1, and marginally significant category representation in the same brain region in Experiment 2. These results further support the validity of our main findings and emphasize the contribution of stimulus representation independent of category representation.

Author response image 3.

Delineating stimulus and category effects using LMEM.  (A) Schematic illustration of this method. (B) Results for late epoch in Experiment 1, showing the fit of each model RDM. (C) Results for early epoch in Experiment 2. (D) Results for late epoch in Experiment 2.

(3) Is it possible that this region of PFC is involved in categorization in particular and not 'control-demanding working memory'? 

We thank the reviewer for raising this possibility. Cognitive control is generally defined as the process by which behavior is flexibly adapted based on task context and goals, and most theories agree that this process occurs within working memory [9, 10]. With this definition, we consider stimulus categorization to be a form of cognitive control, because participants need to adapt the stimulus based on the categorization rule in working memory for subsequent category judgements.  However, in the current study we only used one type of control-demanding working memory task (categorization) to test our hypothesis, and therefore it remains unclear whether the current results in sPCS can generalize to other types of WM control tasks.

We have included a discussion on this issue on lines 572-575 in the revised manuscript.

(4) Some of the figures could be refined to make them more clear:

a.  Figure 4 b/c should have informative titles and y-axis labels.

b.  Figure 5, the flexible vs fixed rule isn't used a ton up to this point - it would help to (also include? Replace?) with something like exp1/exp2 in the legend. It would also help to show the true & orthogonal rule encoding in these different regions (in C, or in a separate panel), especially to the extent that this is a proxy for stimulus encoding.

c.  Figure 6: B and C are very hard to parse right now. (i) The y-axis on B could use a better label. (ii) It would be useful to include an inset of the relevant data panel from fMRI that you are reproducing. (iii) Why aren't there fixed rules for RNN1?

We thank the reviewer for the suggestions and have updated the figures accordingly as following:

Overall I think this is excellent - my feedback is mostly on interpretation and presentation. I think the work itself is really well done, congrats!

References

(1) Glasser, M.F., et al., A multi-modal parcellation of human cerebral cortex. Nature, 2016. 536(7615): p. 171-178.

(2) Yu, Q. and Shim, W.M., Occipital, parietal, and frontal cortices selectively maintain taskrelevant features of multi-feature objects in visual working memory. Neuroimage, 2017. 157: p. 97-107.

(3) Henderson, M.M., Rademaker, R.L., and Serences, J.T., Flexible utilization of spatial- and motor-based codes for the storage of visuo-spatial information. Elife, 2022. 11.

(4) Christophel, T.B., et al., Cortical specialization for attended versus unattended working memory. Nat Neurosci, 2018. 21(4): p. 494-496.

(5) Yu, Q. and Shim, W.M., Temporal-Order-Based Attentional Priority Modulates Mnemonic Representations in Parietal and Frontal Cortices. Cereb Cortex, 2019. 29(7): p. 3182-3192.

(6) Li, S., et al., Neural Representations in Visual and Parietal Cortex Differentiate between Imagined, Perceived, and Illusory Experiences. J Neurosci, 2023. 43(38): p. 6508-6524.

(7) Hu, Y. and Yu, Q., Spatiotemporal dynamics of self-generated imagery reveal a reverse cortical hierarchy from cue-induced imagery. Cell Rep, 2023. 42(10): p. 113242.

(8) Lee, S.H., Kravitz, D.J., and Baker, C.I., Goal-dependent dissociation of visual and prefrontal cortices during working memory. Nat Neurosci, 2013. 16(8): p. 997-9.

(9) Miller, E.K. and Cohen, J.D., An integrative theory of prefrontal cortex function. Annu Rev Neurosci, 2001. 24: p. 167-202.

(10) Badre, D., et al., The dimensionality of neural representations for control. Curr Opin Behav Sci, 2021. 38: p. 20-28.

(11) Flesch, T., et al., Orthogonal representations for robust context-dependent task performance in brains and neural networks. Neuron, 2022. 110(7): p. 1258-1270 e11.

(12) Wang, X.J., Theory of the Multiregional Neocortex: Large-Scale Neural Dynamics and Distributed Cognition. Annu Rev Neurosci, 2022. 45: p. 533-560.

(13) Bellmund, J.L.S., et al., Mnemonic construction and representation of temporal structure in the hippocampal formation. Nat Commun, 2022. 13(1): p. 3395.

Author response:

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

The reviewers suggest a number of experiments and re-analyses to strengthen their claims and enhance the impact of the study. While a number of these are longer term, below is a summary of experiments and analyses recommended by the reviewers that can be accomplished in the shorter term:

(1) Clarification of statistical approaches, quantification, data presentation and description of cerebellar anatomical nomenclature (e.gs. detailed statistical methods for the GEO dataset analysis, FDR correction, quantification in Figs 2-4)

The revised manuscript will provide detailed statistical methods including FDR  correction for GEO dataset analyses and quantification. Please see specific responses to GEO dataset analyses below.

(2) Improved quality of images for select immunostains and in situ hybridization

The revised manuscript will address the quality of the images as indicated by the reviewers.

(3) Include a control group of hGFAP-Cre mice with loxP sites but without Sufu deletion to assess the effects of Cre-induced double-strand breaks on phosphorylated H2AX-DSB signaling.

The breeding scheme we used to generate homozygous SUFU conditional mutants will not generate pups carrying only hGFAP-Cre. Thus, we are unable to compare expression of gH2AX expression in littermates that do not carry loxP sites. The reviewer is correct in pointing out the possibility of Cre recombinase activity inducing double-strand breaks on its own. However, it is likely that any hGFAP-Cre induced double-strand breaks does not sufficiently cause the phenotypes we observed in homozygous mutants (Sufu-cKO) mice because the cerebellum of mice carry heterozygous SUFU mutations (hGFAP-Cre;Sufu-fl/+) do not display the profound cerebellar phenotypes observed in Sufu-cKO mice. We cannot rule out, however, any undetectable abnormalities that could be present which may require further analyses.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

SUFU modulates Sonic hedgehog (SHH) signaling and is frequently mutated in the B-subtype of SHH-driven medulloblastoma. The B-subtype occurs mostly in infants, is often metastatic, and lacks specific treatment. Yabut et al. found that Fgf5 was highly expressed in the B-subtype of SHH-driven medulloblastoma by examining a published microarray expression dataset. They then investigated how Fgf5 functions in the cerebellum of mice that have embryonic Sufu loss of function. This loss was induced using the hGFAP-cre transgene, which is expressed in multiple cell types in the developing cerebellum, including granule neuron precursors (GNPs) derived from the rhombic lip. By measuring the area of Pax6+ cells in the external granule cell layer (EGL) of Sufu-cKO mice at postnatal day 0, they find Pax6+ cells occupy a larger area in the posterior lobe adjacent to the secondary fissure, which is poorly defined. They show that Fgf5 RNA and phosphoErk1/2 immunostaining are also higher in the same disrupted region. Some of the phosphoErk1/2+ cells are proliferative in the Sufu-cKO. Western blot analysis of Gli proteins that modulate SHH signaling found reduced expression and absence of Gli1 activity in the region of cerebellar dysgenesis in Sufu-cKO mice. This suggests the GNP expansion in this region is independent of SHH signaling. Amazingly, intraventricular injection of the FGFR1-2 antagonist AZD4547 from P0-4 and examined histologically at P7 found the treatment restored cytoarchitecture in the cerebella of Sufu-cKO mice. This is further supported by NeuN immunostaining in the internal granule cell layer, which labels mature, non-diving neurons, and KI67 immunostaining, indicating dividing cells, and primarily found in the EGL. The mice were treated beginning at a timepoint when cerebellar cytoarchitecture was shown to be disrupted and it is indistinguishable from control following treatment. Figure 3 presents the most convincing and exciting data in this manuscript.

Sufu-cKO do not readily develop cerebellar tumors. The authors detected phosphorylated H2AX immunostaining, which labels double-strand breaks, in some cells in the EGL in regions of cerebellar dysgenesis in the Sufu-cKO, as was cleaved Caspase 3, a marker of apoptosis. P53, downstream of the double-strand break pathway, the protein was reduced in Sufu-cKO cerebellum. Genetically removing p53 from the Sufu-cKO cerebellum resulted in cerebellar tumors in 2-month old mice. The Sufu;p53-dKO cerebella at P0 lacked clear foliation, and the secondary fissure, even more so than the Sufu-cKO. Fgf5 RNA and signaling (pERK1/2) were also expressed ectopically.

The conclusions of the paper are largely supported by the data, but some data analysis need to be clarified and extended.

(1) The rationale for examining Fgf5 in medulloblastoma is not sufficiently convincing. The authors previously reported that Fgf15 was upregulated in neocortical progenitors of mice with conditional loss of Sufu (PMID: 32737167). In Figure 1, the authors report FGF5 expression is higher in SHH-type medulloblastoma, especially the beta and gamma subtypes mostly found in infants. These data were derived from a genome-wide dataset and are shown without correction for multiple testing, including other Fgfs. Showing the expression of other Fgfs with FDR correction would better substantiate their choice or moving this figure to later in the manuscript as support for their mouse investigations would be more convincing.

To assess FGF5 (ENSG00000138675) expression in MB tissues, we used Geo2R (Barrett et al., 2013) to analyze published human MB subtype expression arrays from accession no. GSE85217 (Cavalli et al., 2017). GEO2R is an interactive web tool that compares expression levels of genes of interest (GOI) between sample groups in the GEO series using original submitter-supplied processed data tables. We entered the GOI Ensembl ID and organized data sets according to age and MB subgroup or MB^SHH subtype classifications. GEO2R results presented gene expression levels as a table ordered by FDR-adjusted (Benjamini & Hochberg) p-values, with significance level cut-off at 0.05, processed by GEO2R’s built-in limma statistical test. Resulting data were subsequently exported into Prism (GraphPad). We generated scatter plots presenting FGF5 expression levels across all MB subgroups (Figure 1A) and MB^SHH subtypes (Figure 1D). We performed additional statistical analyses to compare FGF5 expression levels between MB subgroups and MB^SHH subtypes and graphed these data as violin plots (Figure 1B, 1C, and 1E). For these analyses, we used one-way ANOVA with Holm-Sidak’s multiple comparisons test, single pooled variance. P value ≤0.05 was considered statistically significant. Graphs display the mean ± standard error of the mean (SEM).

Author response image 1.

Comparative expression of FGF ligands, FGF5, FGF10, FGF12, and FGF19, across all MB subgroups. FGF12 expression is not significantly different, while FGF5, FGF10, and FGF19, show distinct upregulation in MB<sup>SHH subgroup (MB^WNT n=70, MB^SHH n=224, MB^GR3 n=143, MB^GR4 n=326).

Expression of the 21 known FGF ligands were also analyzed. Many FGFs did not exhibit differential expression levels in MB^SHH compared to other MB subgroups, such as with FGF12 in Figure 1. FGF5, FGF10, and FGF19 (the human orthologue of mouse FGF15) all showed specific upregulation in MB^SHH compared to other MB subgroups (Author response image 1), supporting our previous observations that FGF15 is a downstream target of SHH signaling (Yabut et al., 2020), as the reviewer pointed out. However, further stratification of MB^SHH patient data revealed that only FGF5 specifically showed upregulation in infants with MBSHH (MB^SHHβ and MB^SHHγ Author response image 2) indicating a more prominent role for FGF5 in the developing cerebellum and driver of MB^SHH tumorigenesis in this dynamic environment.

Author response image 2.

Comparative expression of FGF5, FGF10, and FGF19 in different MB^SHH subtypes. FGF5 specifically show mRNA relative levels above 6 in 81% of MB^SHH infant patient tumors (n=80 MB^SHHα and MB^SHHγ tumors) unlike 35% of MB^SHHα (n=65) or 0% of MB^SHHδ  (n=75) tumors.

(2) The Sufu-cKO cerebellum lacks a clear anchor point at the secondary fissure and foliation is disrupted in the central and posterior lobes. It would be helpful for the authors to review Sudarov & Joyner (PMID: 18053187) for nomenclature specific to the developing cerebellum.

The reviewers are correct that the cerebellar foliation is severely disrupted in central and posterior lobes, as per Sudarov and Joyner (Neural Development 2007). This nomenclature may be referred to describe the regions referred in this manuscript.

(3) The metrics used to quantify cerebellar perimeter and immunostaining are not sufficiently described. It is unclear whether the individual points in the bar graph represent a single section from independent mice, or multiple sections from the same mice. For example, in Figures 2B-D. This also applies to Figure 3C-D.

All quantification were performed from 2-3 20 um cerebellar sections of 3-6 independent mice per genotype analyzed. Individual points in the bar graphs represent the average cell number (quantified from 2-3 sections) from each mice. Figure 2B show data points from n=4 mice per genotype. Figure 2C show data from n=3 mice per genotype. Figure 2D show data from n=6 mice per genotype.  Figure 3C-D show data from n=3 mice per genotype.

(4) The data on Fgf5 RNA expression presented in Figure 2E are not sufficiently convincing. The perimeter and cytoarchitecture of the cerebellum are difficult to see and the higher magnification shown in 2F should be indicated in 2E.

The lack of foliation in Sufu-cKO cerebellum is clear particularly when visualizing the perimeter via DAPI labeling (Figure 2E). The expression area of FGF5 is also visibly larger, given that all images in Figure 2E are presented in the same scale (scale bars = 500 um). 

(5) The data presented in Figure 3 are not sufficiently convincing. The number of cells double positive for pErk and KI67 (Figure 3B) are difficult to see and appear to be few, suggesting the quantification may be unreliable.

We used KI67+ expression to provide a molecular marker of regions to be quantified in both WT and Sufu-cKO sections. Quantification of labeled cells were performed in images obtained by confocal microscopy, enabling imaging of 1-2 um optical slices since Ki67 or pERK expression might not localize within the same cellular compartments. We relied on continuous DAPI nuclear staining to distinguish individual cells in each optical slice and the colocalization of of Ki67 and pERK. All quantification were performed from 2-3 20 um cerebellar sections of 3-6 independent mice per genotype analyzed. Individual points in the bar graphs represent the average cell number (quantified from 2-3 sections) from each mice.

(6) The data presented in Figure 4F-J would be more convincing with quantification. The Sufu;p53-dKO appears to have a thickened EGL across the entire vermis perimeter, and very little foliation, relative to control and single cKO cerebella. This is a more widespread effect than the more localized foliation disruption in the Sufu-cKO. 

We agree with the reviewers that quantification of these phenotypes provide a solid measure of the defects. The phenotypes of Sufu:p53-dKO cerebellum are so profound requiring  in-depth characterization that will be the focus of future studies.

(7) Figure 5 does not convincingly summarize the results. Blue and purple cells in sagittal cartoon are not defined. Which cells express Fgf5 (or other Fgfs) has not been determined. The yellow cells are not defined in relation to the initial cartoon on the left.

The revised manuscript will address this confusion by clearly labeling the cells and their roles in the schematic diagram.

Reviewer #2 (Public Review):

Summary:

Mutations in SUFU are implicated in SHH medulloblastoma (MB). SUFU modulates Shh signaling in a context-dependent manner, making its role in MB pathology complex and not fully understood. This study reports that elevated FGF5 levels are associated with a specific subtype of SHH MB, particularly in pediatric cases. The authors demonstrate that Sufu deletion in a mouse model leads to abnormal proliferation of granule cell precursors (GCPs) at the secondary fissure (region B), correlating with increased Fgf5 expression. Notably, pharmacological inhibition of FGFR restores normal cerebellar development in Sufu mutant mice.

Strengths:

The identification of increased FGF5 in subsets of MB is novel and a key strength of the paper.

Weaknesses:

The study appears incomplete despite the potential significance of these findings. The current paper does not fully establish the causal relationship between Fgf5 and abnormal cerebellar development, nor does it clarify its connection to SUFU-related MB. Some conclusions seem overstated, and the central question of whether FGFR inhibition can prevent tumor formation remains untested.

Reviewer #3 (Public Review):

Summary:

The interaction between FGF signaling and SHH-mediated GNP expansion in MB, particularly in the context of Sufu LoF, has just begun to be understood. The manuscript by Yabut et al. establishes a connection between ectopic FGF5 expression and GNP over-expansion in a late-stage embryonic Sufu LoF model. The data provided links region-specific interaction between aberrant FGF5 signaling with the SHH subtype of medulloblastoma. New data from Yabut et al. suggest that ectopic FGF5 expression correlates with GNP expansion near the secondary fissure in Sufu LoF cerebella. Furthermore, pharmacological blockade of FGF signaling inhibits GNP proliferation. Interestingly, the data indicate that the timing of conditional Sufu deletion (E13.5 using the hGFAP-Cre line) results in different outcomes compared to later deletion (using Math1-cre line, Jiwani et al., 2020). This study provides significant insights into the molecular mechanisms driving GNP expansion in SHH subgroup MB, particularly in the context of Sufu LoF. It highlights the potential of targeting FGF5 signaling as a therapeutic strategy. Additionally, the research offers a model for better understanding MB subtypes and developing targeted treatments.

Strengths:

One notable strength of this study is the extraction and analysis of ectopic FGF5 expression from a subset of MB patient tumor samples. This translational aspect of the study enhances its relevance to human disease. By correlating findings from mouse models with patient data, the authors strengthen the validity of their conclusions and highlight the potential clinical implications of targeting FGF5 in MB therapy.

The data convincingly show that FGFR signaling activation drives GNP proliferation in Sufu, conditional knockout models. This finding is supported by robust experimental evidence, including pharmacological blockade of FGF signaling, which effectively inhibits GNP proliferation. The clear demonstration of a functional link between FGFR signaling and GNP expansion underscores the potential of FGFR as a therapeutic target in SHH subgroup medulloblastoma.

Previous studies have demonstrated the inhibitory effect of FGF2 on tumor cell proliferation in certain MB types, such as the ptc mutant (Fogarty et al., 2006)(Yaguchi et al., 2009). Findings in this manuscript provide additional support suggesting multiple roles for FGF signaling in cerebellar patterning and development.

Weaknesses:

In the GEO dataset analysis, where FGF5 expression is extracted, the reporting of the P-value lacks detail on the statistical methods used, such as whether an ANOVA or t-test was employed. Providing comprehensive statistical methodologies is crucial for assessing the rigor and reproducibility of the results. The absence of this information raises concerns about the robustness of the statistical analysis.

The revised manuscript will include the following detailed explanation of the statistical analyses of the GEO dataset:

For the analysis of expression values of FGF5 (ENSG00000138675), we obtained these values using Geo2R (Barrett et al., 2013), which directly analyze published human MB subtype expression arrays from accession no. GSE85217 (Cavalli et al., 2017). GEO2R is an interactive web tool that compares expression levels of genes of interest (GOI) between sample groups in the GEO series using original submitter-supplied processed data tables. We simply entered the GOI Ensembl ID and organized data sets according to age and MB subgroup or MBSHH subtype classifications. GEO2R results presented gene expression levels as a table ordered by FDR-adjusted (Benjamini & Hochberg) p-values, with significance level cut-off at 0.05, processed by GEO2R’s built-in limma statistical test. Resulting data were subsequently exported into Prism (GraphPad). We generated scatter plots presenting FGF5 expression levels across all MB subgroups (Figure 1A) and MBSHH subtypes (Figure 1D). We performed additional statistical analyses to compare FGF5 expression levels between MB subgroups and MBSHH subtypes and graphed these data as violin plots (Figure 1B, 1C, and 1E). For these analyses, we used one-way ANOVA with Holm-Sidak’s multiple comparisons test, single pooled variance. P value ≤0.05 was considered statistically significant. Graphs display the mean ± standard error of the mean (SEM). Sample sizes were:

Author response table 1.

Another concern is related to the controls used in the study. Cre recombinase induces double-strand DNA breaks within the loxP sites, and the control mice did not carry the Cre transgene (as stated in the Method section), while Sufu-cKO mice did. This discrepancy necessitates an additional control group to evaluate the effects of Cre-induced double-strand breaks on phosphorylated H2AX-DSB signaling. Including this control would strengthen the validity of the findings by ensuring that observed effects are not artifacts of Cre recombinase activity.

The breeding scheme we used to generate homozygous SUFU conditional mutants will not generate pups carrying only hGFAP-Cre. Thus, we are unable to compare expression of gH2AX expression in littermates that do not carry loxP sites. The reviewer is correct in pointing out the possibility of Cre recombinase activity inducing double-strand breaks on its own. However, it is likely that any hGFAP-Cre induced double-strand breaks does not sufficiently cause the phenotypes we observed in homozygous mutants (Sufu-cKO) mice because the cerebellum of mice carry heterozygous SUFU mutations (hGFAP-Cre;Sufu-fl/+) do not display the profound cerebellar phenotypes observed in Sufu-cKO mice. We cannot rule out, however, any undetectable abnormalities that could be present which may require further analyses.

Although the use of the hGFAP-Cre line allows genetic access to the late embryonic stage, this also targets multiple celltypes, including both GNPs and cerebellar glial cells. However, the authors focus primarily on GNPs without fully addressing the potential contributions of neuron-glial interaction. This oversight could limit the understanding of the broader cellular context in which FGF signaling influences tumor development. 

The reviewer is correct in that hGFAP-Cre also targets other cell types, such as cerebellar glial cells, which are generated when Cre-expression has begun. It is possible that cerebellar glial cell development is also compromised in Sufu-cKO mice and may disrupt neuron-glial interaction, due to or independently of FGF signaling. In-depth studies are required to interrogate how loss of SUFU specifically affect development of cerebellar glial cells and influence their cellular interactions in the developing cerebellum.

Recommendations for the authors:

Editorial Comments:

The reviewers suggest a number of steps to improve the manuscript that include additional experiments and a deeper analyses and re-evaluation of existing data. Short of significant new experiments, there appears to be number of straightforward analyses that can improve the study:

(1) Reanalyses of statistical and quantitative approaches used (e.gs FDR correction, cerebellar deficits, GEO analyses.

The revised manuscript will include detailed information on the statistical and quantitative approaches as addressed in our response to the reviewer’s comments.

(2) More clear presentation of qualitative labeling approaches (immunohistochemistry and in situ hybridization).

A detailed description of the protocols used will be included in  the methods section for labeling methods in the revised manuscript.

Reviewer #1 (Recommendations For The Authors):

AZD4547 treatment of the dKO mice would provide more convincing evidence that FGF-targeted treatments could curtail tumor growth in these mice or refute the suggestion that FGF-targeted treatment could prevent tumor growth.

We agree that performing AZD4547 treatment on Sufu-dKO mice will strengthen these studies. However, we are unable to address since these mice are now unavailable. We hope that future studies will address these.

Atoh1 is referred to as Math1 (older nomenclature) and should be corrected.

The revised manuscript will include this change in nomenclature.

Check verb tense throughout the manuscript.

We will edit the manuscript further to check verb tenses prior to submission of the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

Specific Comments:

(1) The identification of increased FGF5 in subsets of MB is novel and a key strength of the paper. However, the causal relationship between FGF5 and MB remains unestablished. Based on the current data, FGF5 can only be considered a biomarker for stratifying MB.

We agree with the reviewer that our studies do not provide direct evidence that FGF5 cause MB. Future investigation focusing on determining if FGF5 inhibition leads to phenotypic rescue will strongly establish the relationship between FGF5 and MB. The reviewer is also correct that our studies reveal that FGF5 acts as a potential biomarker, as we mentioned in the Discussion section.

(2) The upregulation of Fgf5 in Sufu-deficient cerebella is crucial to this study, yet the presented data are unconvincing to support this conclusion. In comparing Fgf5 expression between WT and Sufu mutants (Figures 2E, F and 4I), the cerebellar sections differ significantly, with mutant sections seemingly from a more lateral position. The authors should provide images of mutant sections from more comparable positions to accurately assess the effect of Sufu deficiency on Fgf5 expression. Additionally, the signals in Figure 2F resemble non-specific backgrounds rather than specific RNAscope signals.

The WT and mutant sections analyzed were carefully selected from comparable levels. The abnormal foliation in Sufu-cKO make the mutant sections look like they are from the lateral cerebellum.

Figure 2F (enlarged regions) point to punctate RNAScope signals which is characteristic of this labeling method (see RBFOX3 or GFAP labeling in DAPI-labeled cells in the mouse brain at https://acdbio.com/science/applications/research-areas/neuroscience). The higher number of punctate signals in some, but not all, DAPI-labeled cells in Figure 2F indicate that the FGF5 RNAScope signal is specific.

(3) Jiwani et al. (2020) reported that Fgf8 also expressed in region B of the EGL, is upregulated in Sufu-deficient cerebella and is necessary and sufficient for Sufu mutant GCP proliferation. The current study does not distinguish whether the FGFR inhibitor AZD4547 blocks Fgf5 and Fgf8 function in restoring cerebellar histology in Sufu mutants.

AZD4547 potently inhibits FGFR1, FGFR2, and FGFR3 autophosphorylation (Gavine et al., Cancer Research, 2012). FGF8 is reported to bind to these receptors (Ornitz and Itoh, 2015). Thus, the reviewer is correct that the studies will not distinguish between FGF5 or FGF8 activity. Further investigation on FGF8 expression and the effects of its inhibition in the Sufu-cKO neonatal cerebellum will determine whether tumorigenic processes are driven by either FGF5 or FGF8. Nevertheless, we postulate that FGF5 is exerting a greater effect in activating FGF signaling in the developing cerebellum given that it is highly expressed along the external granule layers of the developing cerebellum (Author response image 3).

Author response image 3.

Expression of FGF5 and FGF8 in the P4 mouse cerebellum (Allen Brain Atlas, https://developingmouse.brain-map.org )

(4) The authors should show whether AZD4547 treatment restores normal Fgf5 expression. Importantly, they need to test whether AZD4547 rescues the proliferation defect observed in Sufu;p53 double mutants.

We agree that performing AZD4547 treatment on Sufu-dKO mice will strengthen these studies. However, we are unable to address since these mice are now unavailable. We hope that future studies will address these.

(5) Jiwani et al. (2020) showed that deleting Sufu with Atoh1-Cre promotes Gli3R and suppresses Gli2 levels, leading to increased cell proliferation and delayed cell cycle exit in the central lobe. The findings of the current study (Supplementary Figure 1) seem to differ from this previous report, yet both studies conclude that Sufu-KO disrupts differentiation. The authors should provide an explanation for this discrepancy.

Our results align completely with the findings by Jiwani et al. (2020). Both studies showed reduced levels of Gli3R, showing nearly 50% reduction, when Sufu is deleted (see Figure 4A-4D in Jiwani et al., 2020).

(6) The hGFAP-Cre mouse line is used to delete Sufu from the cerebellum, but it is not commonly used for GCP-specific deletion. The authors need to provide a reference or more details on the temporal and spatial activity of the Cre line, as the cited paper describes its generation but offers little information on its activity in the developing cerebellum.

We appreciate the reviewer’s reminder to include the reference for the Schuller et al. 2008 paper. This study characterized the hGFAP-Cre temporal and spatial expression in the developing cerebellum, including granule cell precursors. We will include this reference in the revised manuscript.

(7) Based on the provided data, it is difficult to determine which cell types express Fgf5. Given that hGFAP-cre may delete Sufu in other cerebellar cell types, the authors should demonstrate that Fgf5 is expressed in granule cells or granule cell precursors.

Future studies will focus on further characterization of the role of FGF5 in cerebellar development, including the identity cells expressing FGF5. The reviewer is correct in that hGFAP-Cre also targets other cell types and that Sufu deletion in these cells induced ectopic FGF5 expression.

(8) The provided data show an increase in pERK+ cells in GCPs at the secondary fissure. This increase may simply reflect an accumulation of GCPs. It is unconvincing that there is an increase in pERK due to the loss of Sufu.

The reviewer is correct that the increase in GCPs will also result increase the number of pERK+ cells. To control for this, our quantification reflects the number of cells per unit area where Ki67+ cells. With these parameters, we found that there is an increased density of pERK+ cells in a given Ki67+ region. All quantification were performed from 2-3 20 um cerebellar sections of 3-6 independent mice per genotype analyzed. Individual points in the bar graphs represent the average cell number (quantified from 2-3 sections) from each mice.

(9) No data are provided on MB formation in Sufu-cKO; p53- mutants, and it is unknown whether FGFR inhibitors block tumor formation.

We agree that performing AZD4547 treatment on Sufu-dKO mice will strengthen these studies. However, we are unable to address since these mice are now unavailable. We hope that future studies will address these.

(10) The authors frequently mention "preneoplastic lesions" of GCPs in Sufu mutant mice. What evidence supports this claim?

Preneoplastic lesions are defined as cells carrying genetic and phenotypic alterations that show higher risk of malignancy (such as MB) but lack the capacity to grow autonomously in the absence of a secondary factor (Feo et al., 2011). In Sufu-cKO mice, we see abnormally proliferating and behaving granule precursor cells that do not grow autonomously, in the absence of a p53 LOF. The combined deletion of Sufu and p53 transforms these cells to become neoplastic.

(11) Fgf5 is normally expressed in region B. What is its potential function? Does AZD4547 affect normal development? 

Future studies will focus on further characterization of the role of FGF5 in cerebellar development, including the identity cells expressing FGF5. Regarding AZD4547, we did not observe any obvious difference between AZD4547-treated and vehicle-treated cerebelli. These indicate that AZD4547 inhibition of FGFRs under physiologic conditions does not significantly disrupt normal cerebellar development.

(12) Figure 3G: It is unclear which specimens were treated with AZD4547. The authors mention treatment in line 281 but contradict themselves in the figure legend.

We thank the reviewer for pointing out this typo. Cerebellar tissues shown in Figure 3G were all treated with AZD4547. The figure legend will be corrected in the revised manuscript.

(13) Figure 4J: The higher magnification images of the pERK/Ki67 staining appear identical in the control and Sufu;p53-dKO. The authors need to correct the mistake.

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

Minor Comments:

(1) Whenever possible, images comparing WT and mutants should be presented at the same scale within a figure. For example, readers might easily conclude that mutant brains are smaller than controls in Figure 4G.

Unfortunately, because the cerebellum of Sufu;p53-dKO mice are significantly bigger, we are unable to show the whole cerebellum in the same scale in Figure 4G. We wanted to emphasize the significant and abnormal cerebellar growth in this figure.

(2) The figure legend for Supplementary Figure 2 is missing.

Thank you for pointing this out. We will add a figure legend in this Supplementary data in the revised manuscript.

(3) The authors state that the expansion of Pax6+ GNPs in the newborn Sufu-cKO cerebellum (Figure 2) occurs in similar anatomical subregions where infantile MB tumors typically arise (Tan et al., 2018). The cited paper describes more abundant SHH MB in the cerebellar hemisphere. The authors need to elaborate on their statement to clarify this point.

The reviewer is correct in that Tan et al., 2018 observed tumors arising from the cerebellar hemisphere. More specifically, these tumors arise in the posterior/ventral regions of the cerebellar hemispheres (Figure 2 in Tan et al., 2018). Similarly, Sufu-cKO mice have more severe defects in the posterior/ventral regions of the cerebellar hemisphere (Figures 2A and 3F) and therefore corroborate the findings by Tan et al., that abnormal SHH signaling in these regions results in increased sensitivity to MB formation.

Reviewer #3 (Recommendations For The Authors):

Figure1 [Upregulated FGF5 expression in MBS-HH tumors]

- Statistical analysis from the Geo expression dataset does not provide enough detail. At least, the authors should mention whether they have made any adjustments from the default settings and how they extracted/plotted the FGF5 expression (Figure 1BCE).

For the analysis of expression values of FGF5 (ENSG00000138675), we obtained these values using Geo2R (Barrett et al., 2013), which directly analyze published human MB subtype expression arrays from accession no. GSE85217 (Cavalli et al., 2017). GEO2R is an interactive web tool that compares expression levels of genes of interest (GOI) between sample groups in the GEO series using original submitter-supplied processed data tables. We simply entered the GOI Ensembl ID and organized data sets according to age and MB subgroup or MBSHH subtype classifications. GEO2R results presented gene expression levels as a table ordered by FDR-adjusted (Benjamini & Hochberg) p-values, with significance level cut-off at 0.05, processed by GEO2R’s built-in limma statistical test. Resulting data were subsequently exported into Prism (GraphPad). We generated scatter plots presenting FGF5 expression levels across all MB subgroups (Figure 1A) and MB^SHH subtypes (Figure 1D). We performed additional statistical analyses to compare FGF5 expression levels between MB subgroups and MB^SHH subtypes and graphed these data as violin plots (Figure 1B, 1C, and 1E). For these analyses, we used one-way ANOVA with Holm-Sidak’s multiple comparisons test, single pooled variance. P value ≤0.05 was considered statistically significant. Graphs display the mean ± standard error of the mean (SEM). See Author response table 1 for sample sizes.

Figure 3 [Ectopic activation of FGF signaling in the EGL of P0 Sufu-cKO cerebellum]

- Gil1-lz mice reference wrong. Correct Bai CB, et al. 2002

- Generation of Sufu-cKO;Gli1-LacZ triple transgenic mice not described 

- Veh vs. treated not labelled (Figure 3F)

We will address these minor text changes in the revised manuscript. A more detailed description of the generation of Sufu-cKO;Gli1-LacZ triple transgenic will also be included in the Methods section.

Figure 5 [Proposed model]

- In the text, Figure 5 is mistaken for Figure 8. 

We will address these minor text changes in the revised manuscript.

Author Response

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

eLife assessment

This valuable study reports comprehensive multi-omic data on the changes induced in young and aged male mouse tail fibroblasts after treatment with chemical reprogramming factors. The authors claim that chemical reprogramming factors induce changes consistent with a reduction of cellular 'biological' age (e.g., correlations with established aging markers in whole tissues). However, the study relies on previously identified aging markers (instead of aging in the tail fibroblast system itself), and thus, at this stage, the evidence in support of the observed molecular changes truly reflecting changes in biological age in the study system is still incomplete.

Essential revisions

After discussion with reviewers, we believe that the conclusions of the manuscript would be significantly strengthened with the following revisions:

(1) Rather than basing the analysis of age-related markers on public tissue data, it is recommended that authors use their own data on pre-reprogramming fibroblasts to define molecular aging-related markers/signatures specifically for male tail fibroblasts at 4 vs 20 months. This should also always be included in figures as reference points.

We appreciate these helpful comments. Please refer to our responses to Reviewers #1 and #2 concerning these suggestions and the corresponding changes we have made in the revised manuscript.

(2) In general, the methods as written lack the details necessary to fully understand the study/reproduce it independently, notably in terms of data analysis choices (e.g. use of FWER/FDR type correction for multiple testing, use of raw vs normalized RNA counts for PCA, etc).

Thank you for this feedback. We have modified our text to address this issue. Please refer to our responses to Reviewer #1 for the specific changes we have made.

(3) More generally, the authors should better outline the limitations/caveats of their experimental design in the discussion and/or abstract, including the specific cell type and the choice of using only male data (since aging itself is very sex-dimorphic, and the impact of partial reprogramming on aging phenotypes may also be sex-dimorphic).

Thank you for this important feedback. We have now added a section to our Discussion in which we directly address potential limitations of our study concerning sex-specific differences and the cell type used.

Public Reviews:

Reviewer #1:

Summary:

The investigators employed multi-omics approach to show the functional impact of partial chemical reprogramming in fibroblasts from young and aged mice.

Strengths:

Multi-omics data was collected, including epigenome, transcriptome, proteome, phosphoproteome, and metabolome. Different analyses were conducted accordingly, including differential expression analysis, gene set enrichment analysis, transcriptomic and epigenetic clock-based analyses. The impact of partial chemical reprogramming on aging was supported by these multi-source results.

We appreciate the reviewer noting the strength and comprehensiveness of our approach.

Weaknesses:

More experimental data may be needed to further validate current findings.

We thank the reviewer for this suggestion. To further validate our findings, we have proceeded as follows: (1) First, we have investigated the role of Prkaca activation during partial chemical reprogramming with 7c (see updated Fig. 5C, Fig. 5 – figure supplement 1B). By confocal microscopy, we show that partial chemical reprogramming with 7c does not cause Prkaca to localize to mitochondria; rather, its cellular distribution is altered to favor nuclear localization. We also use RNAi to knockdown Prkaca and find that Prkaca is not necessary for mediating the increase in mitochondrial membrane potential upon partial chemical reprogramming with 7c.

(2) We have determined the effect of partial chemical reprogramming with 7c on apoptosis using Annexin V assay (see updated Fig. 5 – figure supplement 1C). We show that during the course of partial chemical reprogramming, the proportion of apoptotic cells steadily increases to about 20 percent.

(3) We have re-analyzed our multi-omics data to determine the molecular differences (e.g. at the epigenome, transcriptome, proteome, and metabolome levels) between fibroblasts isolated from young and old mice (see updated Fig. 2 – figure supplement 1, Fig. 6 – figure supplement 1, and Fig. 7 – figure supplement 2). Additionally, we have updated Fig. 7A to include statistical comparisons of transcriptomic age of 4-month-old and 20-month-old fibroblasts. Finally, we have updated Fig. 3D to include functional enrichment of gene and protein expression levels of aged fibroblasts.

(4) We have more thoroughly characterized the effects of partial chemical reprogramming on the epigenome (see Fig. 7 – figure supplement 3).

(5) Julie Y. Chen was added on as an additional co-author for producing the analyses shown in Fig. 7 – figure supplement 2, and Fig. 7 – figure supplement 3.

Reviewer #2:

The short-term administration of reprogramming factors to partially reprogram cells has gained traction in recent years as a potential strategy to reverse aging in cells and organisms. Early studies used Yamanaka factors in transgenic mice to reverse aging phenotypes, but chemical cocktails could present a more feasible approach for in vivo delivery. In this study, Mitchell et al sought to determine the effects that short-term administration of chemical reprogramming cocktails have on biological age and function. To address this question, they treated young and old mouse fibroblasts with chemical reprogramming cocktails and performed transcriptome, proteome, metabolome, and DNA methylation profiling pre- and post-treatment. For each of these datasets, they identified changes associated with treatment, showing downregulation of some previously identified molecular signatures of aging in both young and old cells. From these data, the authors conclude that partial chemical reprogramming can rejuvenate both young and old fibroblasts.

The main strength of this study is the comprehensive profiling of cells pre- and post-treatment with the reprogramming cocktails, which will be a valuable resource for better understanding the molecular changes induced by chemical reprogramming. The authors highlighted consistent changes across the different datasets that are thought to be associated with aging phenotypes, showing reduction of age-associated signatures previously identified in various tissues. However, from the findings, it remains unclear which changes are functionally relevant in the specific fibroblast system being used. Specifically:

(1) The 4 month and 20 month mouse fibroblasts are designated "young" vs "old" in this study. An important analysis that was not shown for each of the profiled modalities was a comparison of untreated young vs old fibroblasts to determine age-associated molecular changes in this specific model of aging. Then, rather than using aging signatures defined in other tissues, it would be more appropriate to determine whether the chemical cocktails reverted old fibroblasts to a younger state based on the age-associated changes identified in this comparison.

In our study, we have used 4 biological samples per group for young and old untreated fibroblasts, and these samples have been used to calculate the effect of 7c and 2c cocktails on gene expression in each age group. Therefore, the correlation between logFC induced by 7c/2c treatment and logFC between young and old fibroblasts would be biased, since the same untreated samples would be used in both calculations: estimates B-A and C-B will be, on average, negatively correlated even if A, B and C are independent random variables. For this reason, to investigate the effect of cocktails on biological age, we utilized gene expression signatures of aging, estimated based on more than 2,600 samples of different ages from 25 data sources (PMID: 37269831). Notably, our multi-tissue signatures of aging were identified based on data from 17 tissues, including skin. Therefore, these biomarkers seem to represent more reliable and universal molecular mechanisms of aging. Since they have been identified using independent data, the signatures also don’t introduce the statistical bias described above. For these reasons, we think that they are more applicable for the current analysis. To demonstrate that the utilized aging signatures are overall consistent with the changes observed in studied fibroblasts, we performed GSEA-based analysis, testing association between logFC in aged fibroblasts and various signatures of aging and reprogramming (similar to our analysis in Fig. 2E). We found that the changes in aged fibroblasts from the current study demonstrated positive association with the majority of aging signatures (kidney, liver and multi-tissue signatures in mouse and rat) (Fig. 2 – figure supplement 1A) and were negatively associated with signatures of reprogramming. In addition, we characterized functional changes perturbed in untreated aged fibroblasts at the level of gene expression and protein concentrations and observed multiple changes consistent with the aging signatures, such as upregulation of genes and proteins involved in inflammatory response and interferon signaling (Fig. 3D, Fig. 2 – figure supplement 1C). Therefore, changes observed in untreated aged fibroblasts seem to agree with age-related molecular changes identified across mammalian tissues in our previous studies.

We would also like to mention that the epigenetic clocks used in this study consistently show that the fibroblasts from 20-month-old fibroblasts are significantly older than the fibroblasts from 4-month-old mice (Fig. 7B). Moreover, we have revised the manuscript to show that these epigenetic differences between young and old untreated fibroblasts are not due to overall changes in mean DNA methylation (Fig. 7 – figure supplement 2). In contrast, in the revised manuscript, we observe that 7c treatment is reducing the epigenetic age of cells by decreasing mean DNA methylation levels (Fig. 7 – figure supplement 3).

(2) Across all datasets, it appears that the global profiles of young vs old mouse fibroblasts are fairly similar compared to treated fibroblasts, suggesting that the chemical cocktails are not reverting the fibroblasts to a younger state but instead driving them to a different cell state. Similarly, in most cases where specific age-related processes/genes are being compared across untreated and treated samples, no significant differences are observed between young and old fibroblasts.

We agree that our data shows that partial chemical reprogramming seems to induce a similar effect on young and old fibroblasts. In Fig. 2 – figure supplement 1B, the Spearman correlation coefficients for the effects on gene expression in young and old fibroblasts are 0.80 and 0.85 for 2c and 7c, respectively. It is important to note that the effect of partial chemical reprogramming is a magnitude higher (say in terms of number of differentially expressed genes) than the effect of aging in the untreated fibroblasts. Partial chemical reprogramming with 7c, we believe, is pushing the cells to a younger state as a byproduct of producing a different cellular metabolic state with a strong increase in OXPHOS capacity.

(3) Functional validation experiments to confirm that specific changes observed after partial reprogramming are indeed reducing biological age is limited.

Functional validation of rejuvenating interventions is limited in vitro, as cells do not completely maintain their “aged” phenotype once isolated and cultured, and pursuing partial chemical reprogramming in vivo in naturally-aged mice was beyond the scope of the study. One of the best reporters of biological age that are preserved in primary cells in vitro are epigenetic and transcriptomic clocks, which were both utilized in this manuscript to show that 7c treatment, but not 2c, reduces biological age. We show that splicing-related damage is marginally elevated in old fibroblasts compared to young, and that 7c reduces splicing damage by reducing intron retention. Moreover, the epigenetic clocks used in this study show that the 20-month-old fibroblasts are significantly older than the 4-month-old fibroblasts, indicating that the “aged” phenotype is at least partially preserved. Furthermore, according to previous studies (PMIDs: 37269831, 31353263), one of the strongest functional biomarkers of aging is downregulation of mitochondrial function and energy metabolism, including oxidative phosphorylation, while upregulation of these functions is usually associated with extended lifespan in mice. For this reason, we have focused on these pathways in our study and assessed them with functional assays.

(4) Partial reprogramming appears to substantially reduce biological age of the young (4 month) fibroblasts based on the aging signatures used. It is unclear how this result should be interpreted.

This is a caveat of all reprogramming strategies/”anti-aging” interventions developed and tested to date. Currently, there are no genetic or pharmacological methods that target only the “aged” state and not the “young” state as well (i.e. an intervention that would only cause a change in old cells and revert them to a younger state). However, “young” cells in our study and many other studies are still the cells of an intermediate age, as aging appears to begin early during development. Therefore, perhaps unsurprisingly, partial chemical reprogramming seemed to have similar effects on fibroblasts isolated from young and old mice, which is in line with OSK/OSKM reprogramming. These results should be interpreted as follows: partial chemical reprogramming does not depend on the epigenetic state (biological age) of adult cells to induce rejuvenation. We have updated the discussion section of our manuscript accordingly.

Recommendations for the authors:

Reviewer #1:

(1) How was the PCA conducted for RNA-seq data? Were the raw or normalized counts used for PCA?

Normalized counts were used for PCA of the RNA-seq data.

(2) Supplementary Fig 3c, why was the correlation between the red rows and red columns low? Was the color of group messed up? Why was the Pearson correlation used instead of Spearman correlation? Most of the correlation analyses in the manuscript used Spearman correlation.

We thank the reviewer for noticing this mistake. The colors of the groups have now been corrected. Furthermore, to be consistent with the rest of the manuscript, we have performed a Spearman correlation analysis on the normalized proteomics data to evaluate sample-to-sample similarities and updated Fig. 3 – figure supplement 1 accordingly. Overall, the results are similar to those obtained by Pearson correlation.

(3) Were the significant metabolites tested by one-way ANOVA adjusted for family-wise type I error rate? It is surprising that over 50% metabolites were significant.

Yes, the significant metabolites were adjusted for family-wise type I error rate (with a 5% significance threshold) in Fig. 6B.

(4) Missing full names of several abbreviations, such as NIA, RLE, PSI, etc.

Thank you for noticing the missing abbreviations. We have corrected this by writing out the full term in the first instance in which each abbreviation appears.

(5) Methods section may be too long. Some paragraphs could be moved to supplementary text.

eLife does not have a limit to the number of figures or amount of text. Therefore, we have kept the methods section largely unaltered as we feel that they would be helpful to the scientific community.

Reviewer #2:

(1) As discussed in the public review, I would recommend first establishing what differences exist between 4 month and 20 month fibroblasts to identify potential age-related changes in these fibroblasts.

We thank the reviewer for this suggestion. We have now thoroughly characterized the molecular differences between fibroblasts taken from young and old mice at the epigenome, transcriptome, proteome, and metabolome levels. Please refer to previous responses for more specific details.

We have also attempted to establish aging-related differences at the phosphoproteome level, particularly in regards to mitochondrial processes (see figure below), but only GOcc: mitochondrion and GObp: mitochondrial transport come close to being statistically significant (raw p-values of 0.05 and 0.08, respectively) in the control comparison.

Author response image 1.

(2) While the global changes currently highlighted in the study are informative and should remain in the revised manuscript, additional analyses to show which age-related changes identified in point 1 are reverted upon 2c or 7c treatment would better address the question of whether these cocktails revert age-related changes seen in fibroblasts. These analyses should be performed for each dataset (i.e transcriptomic, proteomic, epigenomic, metabolomic) generated.

Thank you for this comment. We have now evaluated the effects of partial chemical reprogramming on the specific molecular differences between fibroblasts isolated from young and old mice (see updated Fig. 2 – figure supplement 1, Fig. 6 – figure supplement 1, Fig. 7 – figure supplement 2, and Fig. 7 – figure supplement 3). For functional enrichment of aged fibroblasts at the gene and protein level, please refer to updated Fig. 3D.

(3) Comparisons between partial reprogramming and OSKM reprogramming signatures are repeatedly made in the paper, but it is not clear from the text whether similarity to OSKM reprogramming signatures is a desired or undesired feature. Since there are likely both rejuvenating and oncogenic aspects of the OSKM signatures, it is unclear what conclusions can be made from these comparisons.

Two central questions of this study were (1) if partial chemical reprogramming could induce cellular rejuvenation, and (2) if so, would it do so by merely chemically activating expression of Yamanaka factors. In this study, we find that 7c, the cocktail that demonstrated the most profound effect on biological age, only minorly upregulates Klf4, downregulates c-Myc, and has no effect on Sox2 or Oct4 expression. Thus, partial chemical reprogramming seems to operate through a mechanism independent of upregulating OSK/OSKM gene expression. This is crucial as it suggests that there are other transcription factors outside of OSKM that can be targeted to induce cellular rejuvenation and reversal of biological age. However, the direct transcriptional targets of partial chemical reprogramming are currently unknown and require further investigation.

Partial reprogramming with OSK/OSKM has several limitations, including low efficiency, oncogenic risk, and differences in the speed of reprogramming according to cell/tissue type. These risks could be inherently tied to the transcription factors OSKM themselves; thus, partial chemical reprogramming, by avoiding strong activation of these genes, could potentially avoid these risks and provide a safer means for reversing biological age in vivo. However, extensive follow-up studies beyond the scope of this manuscript are certainly required to determine this.

We have addressed this comment by modifying the discussion to include these points.

(4) When analyzing the phospho-proteomics data, results are discussed as general changes in phosphorylation of proteins involved in different cellular processes. However, phosphorylation can either activate or inhibit a specific protein, and can depend on the specific residue in a protein that is modified. Different proteins in a cellular process can also respond in opposite directions to phosphorylation. Treating activating and inactivating phosphorylation events separately in describing these results would be more informative.

We agree that an analysis that considers for each specific phosphosite whether it activates or inactivates a particular pathway would in principle be preferable over our current enrichment analysis that only accounts for the increase or decrease in phosphorylation of each site without knowing its biological meaning. However, unfortunately, we think it is currently practically not possible to conduct such an analysis. The proposed analysis would require a database with information on which residues are (de-)phosphorylated when a certain pathway is activated. However, as far as we know, there are currently no databases that link activation or inactivation of specific phosphosites to pathways in repositories like KEGG, HALLMARK, GObp, GOcc, GOmf, Reactome, etc.

Some databases link phosphosites to drugs, diseases and kinases (e.g. PTMsigDB (PMID: 30563849)). However, these authors explicitly state: “We note that we do not capture functional annotations of PTM sites in PTMsigDB, such as activating or inactivating effect on the modified protein.” Furthermore, even in these databases, for the vast majority of the registered phosphosites, the responsible kinases are unknown, especially in mice. In our work, we made use of PhosphoSitePlus for kinase substrate enrichment analysis (see Fig. 5B). Such analyses, where kinase activity is inferred based on activated phosphosites are indeed commonly performed (see PMIDs: 34663829, 37269289, 37585503).

In the absence of a repository that assigns activity to phosphosites, if enrichment analysis is being done for biological pathways, it is standard practice to so without accounting for whether phosphosites are activating or inactivating (see PMID: 34663829), as we have done in our manuscript (Fig. 5A).

Despite the drawbacks, we believe our analysis is relevant, as it demonstrates important biological activity in these pathways uopn 2c/7c treatments as compared to controls. For example, the observed increase in abundance in mitochondrial OXPHOS complexes (Fig. 3E) combined with an increase in general phosphorylation of mitochondrial proteins (Fig. 5A) likely points to an increase mitochondrial activity, although one cannot exclude that some individual phosphorylation events might have inhibitory effects on certain mitochondrial proteins, while others might indicate increases in activity.

(5) For the transcriptomic and epigenetic aging clocks used in Fig 7, significance tests need to be included for untreated 4 month vs 20 month fibroblasts. Particularly for the transcriptional clock, the differences are small and suggest that it may not be a strong aging signature.

We have updated our clock analysis with the most recent versions of the clocks and added statistical significance between 4-month-old and 20-month-old untreated fibroblasts there (Fig. 7A). The difference is statistically significant for the chronological clock. However, when the lifespan-adjusted clock was applied, no statistical significance was observed, suggesting that 20-month-old fibroblasts do not exhibit substantial changes in gene expression associated with decreased healthspan and increased mortality.

(6) For heatmaps shown in Figure 3D and Figure 4, please include untreated 4 month and 20 month fibroblasts as well to determine if pathways being compared are different between young and old fibroblasts.

We have updated Figure 3D with functional enrichment results for aged fibroblasts at gene and protein expression levels, as requested. As for Fig. 4, we explained in our reply to point 1 of Reviewer #2 in the public review why addition of aged fibroblasts there would be biased there. Instead, we have performed GSEA-based association analysis for changes observed in aged fibroblasts and signatures of aging (Fig. 2 – figure supplement 1), confirming that our signatures are overall consistent with patterns of 20-month-old fibroblasts from the current study.

Author response

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

We thank the editor for the eLife assessment and reviewers for their remaining comments. We will address them in this response.

First, we thank eLife for the positive assessment. Regarding the point of visual acuity that is mentioned in this assessment, we understand that this comment is made. It is not an uncommon comment when rodent vision is discussed. However, we emphasize that we took the lower visual acuity of rats and the higher visual acuity of humans into account when designing the human study, by using a fast and eccentric stimulus presentation for humans. As a result, we do not expect a higher discriminability of stimuli in humans. We have described this in detail in our Methods section when describing the procedure in the human experiment:

“We used this fast and eccentric stimulus presentation with a mask to resemble the stimulus perception more closely to that of rats. Vermaercke & Op de Beeck (2012) have found that human visual acuity in these fast and eccentric presentations is not significantly better than the reported visual acuity of rats. By using this approach we avoid that differences in strategies between humans and rats would be explained by such a difference in acuity”

Second, regarding the remaining comment of Reviewer #2 about our use of AlexNet:

While it is indeed relevant to further look into different computational architectures, we chose to not do this within the current study. First, it is a central characteristic of the study procedure that the computational approach and chosen network is chosen early on as it is used to generate the experimental design that animals are tested with. We cannot decide after data collection to use a different network to select the stimuli with which these data were collected. Second, as mentioned in our first response, using AlexNet is not a random choice. It has been used in many previously published vision studies that were relatively positive about the correspondence with biological vision (Cadieu et al., 2014; Groen et al., 2018; Kalfas et al., 2018; Nayebi et al., 2023; Zeman et al., 2020). Third, our aim was not to find a best DNN model for rat vision, but instead examining the visual features that play a role in our complex discrimination task with a model that was hopefully a good enough starting point. The fact that the designs based upon AlexNet resulted in differential and interpretable effects in rats as well as in humans suggests that this computational model was a good start. Comparing the outcomes of different networks would be an interesting next step, and we expect that our approach could work even better when using a network that is more specifically tailored to mimic rat visual processing.

Finally, regarding the choice to specifically chose alignment and concavity as baseline properties, this choice is probably not crucial for the current study. We have no reason to expect rats to have an explicit notion about how a shape is built up in terms of a part-based structure, where alignment relates to the relative position of the parts and concavity is a property of the main base. For human vision it might be different, but we did not focus on such questions in this study.

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

We would like to thank you for giving us the opportunity to submit a revised draft our manuscript. We appreciate the time and effort that you dedicated to providing insightful feedback on our manuscript and are grateful for the valuable comments and improvements on our paper. It helped us to improve our manuscript. We have carefully considered the comments and tried our best to address every one of them. We have added clarifications in the Discussion concerning the type of neural network that we used, about which visual features might play a role in our results as well as clarified the experimental setup and protocol in the Methods section as these two sections were lacking key information points.

Below we provide a response to the public comments and concerns of the reviewers.

Several key points were addressed by at least two reviewers, and we will respond to them first.

A first point concerns the type of network we used. In our study, we used AlexNet to simulate the ventral visual stream and to further examine rat and human performance. While other, more complex neural networks might lead to other results, we chose to work with AlexNet because it has been used in many other vision studies that are published in high impact journals ((Cadieu et al., 2014; Groen et al., 2018; Kalfas et al., 2018; Nayebi et al., 2023; Zeman et al., 2020). We did not try to find a best DNN model for rat vision but instead, we were looking for an explanation of which visual features play a role in our complex discrimination task. We added a consideration to our Discussion addressing why we worked with AlexNet. Since our data will be published on OSF, we encourage to researchers to use our data with other, more complex neural networks and to further investigate this issue.

A second point that was addressed by multiple reviewers concerns the visual acuity of the animals and its impact on their performance. The position of the rat was not monitored in the setup. In a previous study in our lab (Crijns & Op de Beeck, 2019), we investigated the visual acuity of rats in the touchscreen setups by presenting gratings with different cycles per screen to see how it affects their performance in orientation discrimination. With the results from this study and general knowledge about rat visual acuity, we derived that the decision distance of rats lies around 12.5cm from the screen. We have added this paragraph to the Discussion.

A third key point that needs to be addressed as a general point involves which visual features could explain rat and human performance. We reported marked differences between rat and human data in how performance varied across image trials, and we concluded through our computationally informed tests and analyses that rat performance was explained better by lower levels of processing. Yet, we did not investigate which exact features might underlie rat performance. As a starter, we have focused on taking a closer look at pixel similarity and brightness and calculating the correlation between rat/human performance and these two visual features.

We calculated the correlation between the rat performances and image brightness of the transformations. We did this by calculating the difference in brightness of the base pair (brightness base target – brightness base distractor), and subtracting the difference in brightness of every test target-distractor pair for each test protocol (brightness test target – brightness test distractor for each test pair). We then correlated these 287 brightness values (1 for each test image pair) with the average rat performance for each test image pair. This resulted in a correlation of 0.39, suggesting that there is an influence of brightness in the test protocols. If we perform the same correlation with the human performances, we get a correlation of -0.12, suggesting a negative influence of brightness in the human study.

We calculated the correlation between pixel similarity of the test stimuli in relation to the base stimuli with the average performance of the animals on all nine test protocols. We did this by calculating the pixel similarity between the base target with every other testing distractor (A), the pixel similarity between the base target with every other testing target (B), the pixel similarity between the base distractor with every other testing distractor (C) and the pixel similarity between the base distractor with every other testing target (D). For each test image pair, we then calculated the average of (A) and (D), and subtracted the average of (C) and (B) from it. We correlated these 287 values (one for each image pair) with the average rat performance on all test image pairs, which resulted in a correlation of 0.34, suggesting an influence of pixel similarity in rat behaviour. Performing the same correlation analysis with the human performances results in a correlation of 0.12.

We have also addressed this in the Discussion of the revised manuscript. Note that the reliability of the rat data was 0.58, clearly higher than the correlations with brightness and pixel similarity, thus these features capture only part of the strategies used by rats.

We have also responded to all other insightful suggestions and comments of the reviewers, and a point-by-point response to the more major comments will follow now.  

Reviewer #1, general comments:

The authors should also discuss the potential reason for the human-rat differences too, and importantly discuss whether these differences are coming from the rather unusual approach of training used in rats (i.e. to identify one item among a single pair of images), or perhaps due to the visual differences in the stimuli used (what were the image sizes used in rats and humans?). Can they address whether rats trained on more generic visual tasks (e.g. same-different, or category matching tasks) would show similar performance as humans?

The task that we used is typically referred to as a two-alternative forced choice (2AFC). This is a simple task to learn. A same-different task is cognitively much more demanding, also for artificial neural networks (see e.g. Puebla & Bowers, 2022, J. Vision). A one-stimulus choice task (probably what the reviewer refers to with category matching) is known to be more difficult compared to 2AFC, with a sensitivity that is predicted to be Sqrt(2) lower according to signal detection theory (MacMillan & Creelman, 1991). We confirmed this prediction empirically in our lab (unpublished observations). Thus, we predict that rats perform less good in the suggested alternatives, potentially even (in case of same-different) resulting in a wider performance gap with humans.

I also found that a lot of essential information is not conveyed clearly in the manuscript. Perhaps it is there in earlier studies but it is very tedious for a reader to go back to some other studies to understand this one. For instance, the exact number of image pairs used for training and testing for rats and humans was either missing or hard to find out. The task used on rats was also extremely difficult to understand. An image of the experimental setup or a timeline graphic showing the entire trial with screenshots would have helped greatly.

All the image pairs used for training and testing for rats and humans are depicted in Figure 1 (for rats) and Supplemental Figure 6 (for humans). For the first training protocol (Training), only one image pair was shown, with the target being the concave object with horizontal alignment of the spheres. For the second training protocol (Dimension learning), three image pairs were shown, consisting of the base pair, a pair which differs only in concavity, and a pair which differs only in alignment. For the third training protocol (Transformations) and all testing protocols, all combination of targets and distractors were presented. For example, in the Rotation X protocol, the stimuli consisted of 6 targets and 6 distractors, resulting in a total of 36 image pairs for this protocol. The task used on rats is exactly as shown in Figure 1. A trial started with two blank screens. Once the animal initiated a trial by sticking its head in the reward tray, one stimulus was presented on each screen. There was no time limit and so the stimuli remained on the screen until the animal made a decision. If the animal touched the target, it received a sugar pellet as reward and a ITI of 20s started. If the animal touched the distractor, it did not receive a sugar pellet and a time-out of 5s started in addition to the 20s ITI.

We have clarified this in the manuscript.

The authors state that the rats received random reward on 80% of the trials, but is that on 80% of the correctly responded trials or on 80% of trials regardless of the correctness of the response? If these are free choice experiments, then the task demands are quite different. This needs to be clarified. Similarly, the authors mention that 1/3 of the trials in a given test block contained the old base pair - are these included in the accuracy calculations?

The animals receive random reward on 80% on all testing trials with new stimuli, regardless of the correctness of the response. This was done to ensure that we can measure true generalization based upon learning in the training phase, and that the animals do not learn/are not trained in these testing stimuli. For the trials with the old stimuli (base pair), the animals always received real reward (reward when correct; no reward in case of error).

The 1/3rd trials with old stimuli are not included in the accuracy calculations but were used as a quality check/control to investigate which sessions have to be excluded and to assure that the rats were still doing the task properly. We have added this in the manuscript.

The authors were injecting noise with stimuli to cDNN to match its accuracy to rat. However, that noise potentially can interacted with the signal in cDNN and further influence the results. That could generate hidden confound in the results. Can they acknowledge/discuss this possibility?

Yes, adding noise can potentially interact with the signal and further influence the results. Without noise, the average training data of the network would lie around 100% which would be unrealistic, given the performances of the animals. To match the training performance of the neural networks with that of the rats, we added noise 100 times and averaged over these iterations (cfr. (Schnell et al., 2023; Vinken & Op de Beeck, 2021)).  

Reviewer #2, weaknesses:

1) There are a few inconsistencies in the number of subjects reported. Sometimes 45 humans are mentioned and sometimes 50. Probably they are just typos, but it's unclear.

Thank you for your feedback. We have doublechecked this and changed the number of subjects where necessary. We collected data from 50 human participants, but had to exclude 5 of them due to low performance during the quality check (Dimension learning) protocols. Similarly, we collected data from 12 rats but had to exclude one animal because of health issues. All these data exclusion steps were mentioned in the Methods section of the original version of the manuscript, but the subject numbers were not always properly adjusted in the description in the Results section. This is now corrected.

2) A few aspects mentioned in the introduction and results are only defined in the Methods thus making the manuscript a bit hard to follow (e.g. the alignment dimension), thus I had to jump often from the main text to the methods to get a sense of their meaning.

Thank you for your feedback. We have clarified some aspects in the Introduction, such as the alignment dimension.

4) Many important aspects of the task are not fully described in the Methods (e.g. size of the stimuli, reaction times and basic statistics on the responses).

We have added the size of the stimuli to the Methods section and clarified that the stimuli remained on the screen until the animals made a choice. Reaction time in our task would not be interpretable given that stimuli come on the screen when the animal initiates a trial with its back to the screen. Therefore we do not have this kind of information.

Reviewer #1

• Can the authors show all the high vs zero and zero vs high stimulus pairs either in the main or supplementary figures? It would be instructive to know if some other simple property covaried between these two sets.

In Figure 1, all images of all protocols are shown. For the High vs. Zero and Zero vs. High protocols, we used a deep neural network to select a total of 7 targets and 7 distractors. This results in 49 image pairs (every combination of target-distractor).

• Are there individual differences across animals? It would be useful for the authors to show individual accuracy for each animal where possible.

We now added individual rat data for all test protocols – 1 colour per rat, black circle = average. We have added this picture to the Supplementary material (Supplementary Figure 1).

• Figure 1 - it was not truly clear to me how many image pairs were used in the actual experiment. Also, it was very confusing to me what was the target for the test trials. Additionally, authors reported their task as a categorisation task, but it is a discrimination task.

Figure 1 shows all the images that were used in this study. Every combination of every target-distractor in each protocol (except for Dimension learning) was presented to the animals. For example in Rotation X, the test stimuli as shown in Fig. 1 consisted of 6 targets and 6 distractors, resulting in a total of 36 image pairs for this test protocol.

In each test protocol, the target corresponded to the concave object with horizontally attached spheres, or the object from the pair that in the stimulus space was closed to this object. We have added this clarification in the Introduction: “We started by training the animals in a base stimulus pair, with the target being the concave object with horizontally aligned spheres. Once the animals were trained in this base stimulus pair, we used the identity-preserving transformations to test for generalization.” as well as in the caption of Figure 1. We have changed the term “categorisation task” to “discrimination task” throughout the manuscript.

• Figure 2 - what are the red and black lines? How many new pairs are being tested here? Panel labels are missing (a/b/c etc)

We have changed this figure by adding panel labels, and clarifying the missing information in the caption. All images that were shown to the animals are presented on this figure. For Dimension Learning, only three image pairs were shown (base pair, concavity pair, alignment pair) and for the Transformations protocol, every combination of every target and distractor were shown, i.e. 25 image pairs in total.

• Figure 3 - last panel: the 1st and 2nd distractor look identical.

We understand your concern as these two distractors indeed look quite similar. They are different however in terms of how they are rotated along the x, y and z axes (see Author response image 1 for a bigger image of these two distractors). The similarity is due to the existence of near-symmetry in the object shape which causes high self-similarity for some large rotations.

Author response image 1.

• Line 542 – authors say they have ‘concatenated’ the performance of the animals, but do they mean they are taking the average across animals?

It is both. In this specific analysis we calculated the performance of the animals, which was indeed averaged across animals, per test protocol, per stimulus pair. This resulted in 9 arrays (one for each test protocol) of several performances (1 for each stimulus pair). These 9 arrays were concatenated by linking them together in one big array (i.e. placing them one after the other). We did the same concatenation with the distance to hyperplane of the network on all nine test protocols. These two concatenated arrays with 287 values each (one with the animal performance and one with the DNN performance) were correlated.

• Line 164 - What are these 287 image pairs - this is not clear.

The 287 image pairs correspond to all image pairs of all 9 test protocols: 36 (Rotation X) + 36 (Rotation Y) + 36 (Rotation Z) + 4 (Size) + 25 (Position) + 16 (Light location) + 36 (Combination Rotation) + 49 (Zero vs. high) + 49 (High vs. zero) = 287 image pairs in total. We have clarified this in the manuscript.

• Line 215 - Human rat correlation (0.18) was comparable to the best cDNN layer correlation. What does this mean?

The human rat correlation (0.18) was closest to the best cDNN layer - rat correlation (about 0.15). In the manuscript we emphasize that rat performance is not well captured by individual cDNN layers.  

Reviewer #2

Major comments

• In l.23 (and in the methods) the authors mention 50 humans, but in l.87 they are 45. Also, both in l.95 and in the Methods the authors mention "twelve animals" but they wrote 11 elsewhere (e.g. abstract and first paragraph of the results).

In our human study design, we introduced several Dimension learning protocols. These were later used as a quality check to indicate which participants were outliers, using outlier detection in R. This resulted in 5 outlying human participants, and thus we ended with a pool of 45 human participants that were included in the analyses. This information was given in the Methods section of the original manuscript, but we did not mention the correct numbers everywhere. We have corrected this in the manuscript. We also changed the number of participants (humans and rats) to the correct one throughout the entire manuscript.

• At l.95 when I first met the "4x4 stimulus grid" I had to guess its meaning. It would be really useful to see the stimulus grid as a panel in Figure 1 (in general Figures S1 and S4 could be integrated as panels of Figure 1). Also, even if the description of the stimulus generation in the Methods is probably clear enough, the authors might want to consider adding a simple schematic in Figure 1 as well (e.g. show the base, either concave or convex, and then how the 3 spheres are added to control alignment).

We have added the 4x4 stimulus grid in the main text.

• There is also another important point related to the choice of the network. As I wrote, I find the overall approach very interesting and powerful, but I'm actually worried that AlexNet might not be a good choice. I have experience trying to model neuronal responses from IT in monkeys, and there even the higher layers of AlexNet aren't that helpful. I need to use much deeper networks (e.g. ResNet or GoogleNet) to get decent fits. So I'm afraid that what is deemed as "high" in AlexNet might not be as high as the authors think. It would be helpful, as a sanity check, to see if the authors get the same sort of stimulus categories when using a different, deeper network.

We added a consideration to the manuscript about which network to use (see the Discussion): “We chose to work with Alexnet, as this is a network that has been used as a benchmark in many previous studies (e.g. (Cadieu et al., 2014; Groen et al., 2018; Kalfas et al., 2018; Nayebi et al., 2023; Zeman et al., 2020)), including studies that used more complex stimuli than the stimulus space in our current study. […] . It is in line with the literature that a typical deep neural network, AlexNet and also more complex ones, can explain human and animal behaviour to a certain extent but not fully. The explained variance might differ among DNNs, and there might be DNNs that can explain a higher proportion of rat or human behaviour. Most relevant for our current study is that DNNs tend to agree in terms of how representations change from lower to higher hierarchical layers, because this is the transformation that we have targeted in the Zero vs. high and High vs. zero testing protocols. (Pinto et al., 2008) already revealed that a simple V1-like model can sometimes result in surprisingly good object recognition performance. This aspect of our findings is also in line with the observation of Vinken & Op de Beeck (2021) that the performance of rats in many previous tasks might not be indicative of highly complex representations. Nevertheless, there is still a relative difference in complexity between lower and higher levels in the hierarchy. That is what we capitalize upon with the Zero vs. high and High vs. zero protocols. Thus, it might be more fruitful to explicitly contrast different levels of processing in a relative way rather than trying to pinpoint behaviour to specific levels of processing.”

• The task description needs way more detail. For how long were the stimuli presented? What was their size? Were the positions of the stimuli randomized? Was it a reaction time task? Was the time-out used as a negative feedback? In case, when (e.g. mistakes or slow responses)? Also, it is important to report some statistics about the basic responses. What was the average response time, what was the performance of individual animals (over days)? Did they show any bias for a particular dimension (either the 2 baseline dimensions or the identity preserving ones) or side of response? Was there a correlation within animals between performance on the baseline task and performance on the more complex tasks?

Thank you for your feedback. We have added more details to the task description in the manuscript.

The stimuli were presented on the screens until the animals reacted to one of the two screens. The size of the stimuli was 100 x 100 pixel. The position of the stimuli was always centred/full screen on the touchscreens. It was not a reaction time task and we also did not measure reaction time.

• Related to my previous comment, I wonder if the relative size/position of the stimulus with respect to the position of the animal in the setup might have had an impact on the performance, also given the impact of size shown in Figure 2. Was the position of the rat in the setup monitored (e.g. with DeepLabCut)? I guess that on average any effect of the animal position might be averaged away, but was this actually checked and/or controlled for?

The position of the rat was not monitored in the setup. In a previous study from our lab (Crijns & Op de Beeck, 2019), we investigated the visual acuity of rats in the touchscreen setups by presenting gratings with different cycles per screen to see how it affects their performance in orientation discrimination. With the results from this study and general knowledge about rat visual acuity, we derived that the decision distance of rats lies around 12.5cm from the screen. We have added this to the discussion.

Minor comments

• l.33 The sentence mentions humans, but the references are about monkeys. I believe that this concept is universal enough not to require any citation to support it.

Thank you for your feedback. We have removed the citations.

• This is very minor and totally negligible. The acronymous cDNN is not that common for convents (and it's kind of similar to cuDNN), it might help clarity to stick to a more popular acronymous, e.g. CNN or ANN. Also, given that the "high" layers used for stimulus selection where not convolutional layers after all (if I'm not mistaken).

Thank you for your feedback. We have changed the acronym to ‘CNN’ in the entire manuscript.

• In l.107-109 the authors identified a few potential biases in their stimuli, and they claim these biases cannot explain the results. However, the explanation is given only in the next pages. It might help to mention that before or to move that paragraph later, as I was just wondering about it until I finally got to the part on the brightness bias.

We expanded the analysis of these dimensions (e.g. brightness) throughout the manuscript.

• It would help a lot the readability to put also a label close to each dimension in Figures 2 and 3. I had to go and look at Figure S4 to figure that out.

Figures 2 and 3 have been updated, also including changes related to other comments.

• In Figure 2A, please specify what the red dashed line means.

We have edited the caption of Figure 2: “Figure 2 (a) Results of the Dimension learning training protocol. The black dashed horizontal line indicates chance level performance and the red dashed line represents the 80% performance threshold. The blue circles on top of each bar represent individual rat performances. The three bars represent the average performance of all animals on the old pair (Old), the pair that differs only in concavity (Conc) and on the pair that differs only in alignment (Align). (b) Results of the Transformations training protocol. Each cell of the matrix indicates the average performance per stimulus pair, pooled over all animals. The columns represent the distractors, whereas the rows separate the targets. The colour bar indicates the performance correct. ”

• Related to that, why performing a binomial test on 80%? It sounds arbitrary.

We performed the binomial test on 80% as 80% is our performance threshold for the animals

• The way the cDNN methods are introduced makes it sound like the authors actually fine-tuned the weights of AlexNet, while (if I'm not mistaken), they trained a classifier on the activations of a pre-trained AlexNet with frozen weights. It might be a bit confusing to readers. The rest of the paragraph instead is very clear and easy to follow.

We think the most confusing sentence was “ Figure 7 shows the performance of the network after training the network on our training stimuli for all test protocols. “ We changed this sentence to “ Figure 8 shows the performance of the network for each of the test protocols after training classifiers on the training stimuli using the different DNN layers.“

Reviewer #3

Main recommendations:

Although it may not fully explain the entire pattern of visual behavior, it is important to discuss rat visual acuity and its impact on the perception of visual features in the stimulus set.

We have added a paragraph to the Discussion that discusses the visual acuity of rats and its impact on perceiving the visual features of the stimuli.

The authors observed a potential influence of image brightness on behavior during the dimension learning protocol. Was there a correlation between image brightness and the subsequent image transformations?

We have added this to the Discussion: “To further investigate to which visual features the rat performance and human performance correlates best with, we calculated the correlation between rat performance and pixel similarity of the test image pairs, as well as the correlation between rat performance and brightness in the test image pairs. Here we found a correlation of 0.34 for pixel similarity and 0.39 for brightness, suggesting that these two visual features partly explain our results when compared to the full-set reliability of rat performance (0.58). If we perform the same correlation with the human performances, we get a correlation of 0.12 for pixel similarity and -0.12 for brightness. With the full-set reliability of 0.58 (rats) and 0.63 (humans) in mind, this suggests that even pixel similarity and brightness only partly explain the performances of rats and humans.”

Did the rats rely on consistent visual features to perform the tasks? I assume the split-half analysis was on data pooled across rats. What was the average correlation between rats? Were rats more internally consistent (split-half within rat) than consistent with other rats?

The split-half analysis was indeed performed on data pooled across rats. We checked whether rats are more internally consistent by comparing the split-half within correlations with the split-half between correlations. For the split-half within correlations, we split the data for each rat in two subsets and calculated the performance vectors (performance across all image pairs). We then calculated the correlation between these two vectors for each animal. To get the split-half between correlation, we calculated the correlation between the performance vector of every subset data of every rat with every other subset data from the other rats. Finally, we compared for each animal its split-half within correlation with the split-half between correlations involving that animal. The result of this paired t-test (p = 0.93, 95%CI [-0.09; 0.08]) suggests that rats were not internally more consistent.

Discussion of the cDNN performance and its relation to rat behavior could be expanded and clarified in several ways:

• The paper would benefit from further discussion regarding the low correlations between rat behavior and cDNN layers. Is the main message that cDNNs are not a suitable model for rat vision? Or can we conclude that the peak in mid layers indicates that rat behavior reflects mid-level visual processing? It would be valuable to explore what we currently know about the organization of the rat visual cortex and how applicable these models are to their visual system in terms of architecture and hierarchy.

We added a consideration to the manuscript about which network to use (see Discussion).

• The cDNN exhibited above chance performance in various early layers for several test protocols (e.g., rotations, light location, combination rotation). Does this limit the interpretation of the complexity of visual behavior required to perform these tasks?

This is not uncommon to find. Pinto et al. (2008) already revealed that a simple V1-like model can sometimes result in surprisingly good object recognition performance. This aspect of our findings is also in line with the observation of Vinken & Op de Beeck (2021) that the performance of rats in many previous tasks might not be indicative of highly complex representations. Nevertheless, there is still a relative difference in complexity between lower and higher levels in the hierarchy. That is what we capitalize upon with the High vs zero and the Zero vs high protocols. Thus, it might be more fruitful to explicitly contrast different levels of processing in a relative way rather than trying to pinpoint behavior to specific levels of processing. This argumentation is added to the Discussion section.

• How representative is the correlation profile between cDNN layers and behavior across protocols? Pooling stimuli across protocols may be necessary to obtain stable correlations due to relatively modest sample numbers. However, the authors could address how much each individual protocol influences the overall correlations in leave-one-out analyses. Are there protocols where rat behavior correlates more strongly with higher layers (e.g., when excluding zero vs. high)?

We prefer to base our conclusions mostly on the pooled analyses rather than individual protocols. As the reviewer also mentions, we can expect that the pooled analyses will provide the most stable results. For information, we included leave-one-out analyses in the supplemental material. Excluding the Zero vs. High protocol did not result in a stronger correlation with the higher layers. It was rare to see correlations with higher layers, and in the one case that we did (when excluding High versus zero) the correlations were still higher in several mid-level layers.

Author response image 2.

• The authors hypothesize that the cDNN results indicate that rats rely on visual features such as contrast. Can this link be established more firmly? e.g., what are the receptive fields in the layers that correlate with rat behavior sensitive to?

This hypothesis was made based on previous in-lab research ((Schnell et al., 2023) where we found rats indeed rely on contrast features. In this study, we performed a face categorization task, parameterized on contrast features, and we investigated to what extent rats use contrast features to perform in a face categorization task. Similarly as in the current study, we used a DNN that as trained and tested on the same stimuli as the animals to investigate the representations of the animals. There, we found that the animals use contrast features to some extent and that this correlated best with the lower layers of the network. Hence, we would say that the lower layers correlate best with rat behaviour that is sensitive to contrast. Earlier layers of the network include local filters that simulate V1-like receptive fields. Higher layers of the network, on the other hand, are used for object selectivity.

• There seems to be a disconnect between rat behavior and the selection of stimuli for the high (zero) vs. zero (high) protocols. Specifically, rat behavior correlated best with mid layers, whereas the image selection process relied on earlier layers. What is the interpretation when rat behavior correlates with higher layers than those used to select the stimuli?

We agree that it is difficult to pinpoint a particular level of processing, and it might be better to use relative terms: lower/higher than. This is addressed in the manuscript by the edit in response to three comments back.

• To what extent can we attribute the performance below the ceiling for many protocols to sensory/perceptual limitations as opposed to other factors such as task structure, motivation, or distractibility?

We agree that these factors play a role in the overall performance difference. In Figure 5, the most right bar shows the percentage of all animals (light blue) vs all humans (dark blue) on the old pair that was presented during the testing protocol. Even here, the performance of the animals was lower than humans, and this pattern extended to the testing protocols as well. This was most likely due to motivation and/or distractibility which we know can happen in both humans and rats but affects the rat results more with our methodology.

Minor recommendations:

• What was the trial-to-trial variability in the distance and position of the rat's head relative to the stimuli displayed on the screen? Can this variability be taken into account in the size and position protocols? How meaningful is the cDNN modelling of these protocols considering that the training and testing of the model does not incorporate this trial-to-trial variability?

We have no information on this trial-to-trial variability. We have information though on what rats typically do overall from an earlier paper that was mentioned in response to an earlier comment (Crijns et al.).

We have added a disclaimer in the Discussion on our lack of information on trial-to-trial variability.

• Several of the protocols varied a visual feature dimension (e.g., concavity & alignment) relative to the base pair. Did rat performance correlate with these manipulations? How did rat behavior relate to pixel dissimilarity, either between target and distractor or in relation to the trained base pair?

We have added this to the Discussion. See also our general comments in the Public responses.

• What could be the underlying factor(s) contributing to the difference in accuracy between the "small transformations" depicted in Figure 2 and some of the transformations displayed in Figure 3? In particular, it seems that the variability of targets and distractors is greater for the "small transformations" in Figure 2 compared to the rotation along the y-axis shown in Figure 3.

There are several differences between these protocols. Before considering the stimulus properties, we should take into account other factors. The Transformations protocol was a training protocol, meaning that the animals underwent several sessions in this protocol, always receiving real reward during the trials, and only stopping once a high enough performance was reached. For the protocols in Figure 3, the animals were also placed in these protocols for multiple sessions in order to obtain enough trials, however, the difference here is that they did not receive real reward and testing was also stopped if performance was still low.

• In Figure 3, it is unclear which pairwise transformation accuracies were above chance. It would be helpful if the authors could indicate significant cells with an asterisk. The scale for percentage correct is cut off at 50%. Were there any instances where the behaviors were below 50%? Specifically, did the rats consistently choose the wrong option for any of the pairs? It would be helpful to add "old pair", "concavity" and "alignment" to x-axis labels in Fig 2A .

We have added “old”, “conc” and “align” to the x-axis labels in Figure 2A.

• Considering the overall performance across protocols, it seems overstated to claim that the rats were able to "master the task."

When talking about “mastering the task”, we talk about the training protocols where we aimed that the animals would perform at 80% and not significantly less. We checked this throughout the testing protocols as well, where we also presented the old pair as quality control, and their performance was never significantly lower than our 80% performance threshold on this pair, suggesting that they mastered the task in which they were trained. To avoid discussion on semantics, we also rephrased “master the task” into “learn the task”.

• What are the criteria for the claim that the "animal model of choice for vision studies has become the rodent model"? It is likely that researchers in primate vision may hold a different viewpoint, and data such as yearly total publication counts might not align with this claim.

Primate vision is important for investigating complex visual aspects. With the advancements in experimental techniques for rodent vision, e.g. genetics and imaging techniques as well as behavioural tasks, the rodent model has become an important model as well. It is not necessarily an “either” or “or” question (primates or rodents), but more a complementary issue: using both primates and rodents to unravel the full picture of vision.

We have changed this part in the introduction to “Lately, the rodent model has become an important model in vision studies, motivated by the applicability of molecular and genetic tools rather than by the visual capabilities of rodents”.

• The correspondence between the list of layers in Supplementary Tables 8 and 9 and the layers shown in Figures 4 and 6 could be clarified.

We have clarified this in the caption of Figure 7

• The titles in Figures 4 and 6 could be updated from "DNN" to "cDNN" to ensure consistency with the rest of the manuscript.

Thank you for your feedback. We have changed the titles in Figures 4 and 6 such that they are consistent with the rest of the manuscript.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

(1) Potential bleed-over across frequencies in the spectral domain is a major concern for all of the results in this paper. The fact that alpha power, 36Hz and 40Hz frequency-tagged amplitude and 4Hz intermodulation frequency power is generally correlated with one another amplifies this concern. The authors are attaching specific meaning to each of these frequencies, but perhaps there is simply a broadband increase in neural activity when anticipating an auditory target compared to a visual target?

We appreciate the reviewer’s insightful comment regarding the potential bleed-over across frequencies in the spectral domain. We fully acknowledge that the trade-off between temporal and frequency resolution is a challenge, particularly given the proximity of the frequencies we are examining.

To address this concern, we performed additional analyses to investigate whether there is indeed a broadband increase in neural activity when anticipating an auditory target as compared to a visual target, as opposed to distinct frequency-specific effects. Our results show that the bleed-over between frequencies is minimal and does not significantly affect our findings. Specifically, we repeated the analyses using the same filter and processing steps for the 44 Hz frequency. At this frequency, we did not observe any significant differences between conditions.

These findings suggest that the effects we report are indeed specific to the 40 Hz frequency band and not due to a general broadband increase in neural activity. We hope this addresses the reviewer’s concern and strengthens the validity of our frequency-specific results. We have now added this analysis to the methods section of our manuscript.

Line 730: To confirm that 4 Hz is a sufficient distance between tagging frequencies, we repeated to analysis for 43.5 to 44.5. We found no indication of frequency-bleeding over, as the effects observed at 40 Hz, were not present at 44 Hz (see SUPPL Fig. 11).

We do, however, not specifically argue against the possibility of a broadband increase in sensory processing when anticipating an auditory compared to a visual target. But even a broadband-increase would directly contradict the alpha inhibition hypothesis, which poses that an increase in alpha completely disengage the whole cortex. We have made this clearer in the text now.

Line 491: As auditory targets were significantly more difficult than visual targets in our first study and of comparable difficulty in our second study, these results strongly speak to a vigilance increase of sensory processing independent of modality and an inability to selectively disengage one sensory modality in anticipation of a demanding task. This view is consistent with previous work in which visual SSEPs elicited by irrelevant background stimulation increased with task load in an auditory discrimination task (Jacoby et al., 2012).

(2) Moreover, 36Hz visual and 40Hz auditory signals are expected to be filtered in the neocortex. Applying standard filters and Hilbert transform to estimate sensory evoked potentials appears to rely on huge assumptions that are not fully substantiated in this paper. In Figure 4, 36Hz "visual" and 40Hz "auditory" signals seem largely indistinguishable from one another, suggesting that the analysis failed to fully demix these signals.

We appreciate the reviewer’s insightful concern regarding the filtering and demixing of the 36 Hz visual and 40 Hz auditory signals, and we share the same reservations about the reliance on standard filters and the Hilbert transform method.

To address this, we would like to draw attention to SUPPL Fig. 11, which demonstrates that a 4 Hz difference is sufficient to effectively demix the signals using our chosen filtering and Hilbert transform approach. We argue that the reason the 36 Hz visual and 40 Hz auditory signals show similar topographies lies not in incomplete demixing but rather in the possibility that this condition difference reflects sensory integration, rather than signal contamination.

This interpretation is further supported by our findings with the intermodulation frequency at 4 Hz, which also suggests cross-modal integration. Furthermore, source localization analysis revealed that the strongest condition differences were observed in the precuneus, an area frequently associated with sensory integration processes. We have now expanded on this in the discussion section to better clarify this point.

Line 578: Previous research has shown that simultaneous frequency-tagging at multiple frequencies can evoke a response at the intermodulation frequency (f1 – f2), which in multimodal settings is thought to reflect cross-modal integration (Drijvers et al., 2021). This concept aligns closely with our findings, where increased vigilance in the sensory system, prompted by anticipation of a difficult auditory target, resulted in an increase in the intermodulation frequency. Similarly, our data shows that visual signal enhancement was localized in the precuneus, further supporting the role of this region in sensory integration (Al-Ramadhani et al., 2021; Xie et al., 2019).

(3) The asymmetric results in the visual and auditory modalities preclude a modality-general conclusion about the function of alpha. However, much of the language seems to generalize across sensory modalities (e.g., use of the term 'sensory' rather than 'visual').

We agree that in some cases we have not made a sufficient distinction between visual and sensory. We have now made sure, that when using ‘sensory’, we either describe overall theories, which are not visual-exclusive or refer to the possibility of a broad sensory increase. However, when directly discussing our results and the interpretation thereof, we now use ‘visual’.

(4) In this vein, some of the conclusions would be far more convincing if there was at least a trend towards symmetry in source-localized analyses of MEG signals. For example, how does alpha power in primary auditory cortex (A1) compare when anticipating auditory vs visual target? What do the frequency tagged visual and auditory responses look like when just looking at primary visual cortex (V1) or A1?

We thank the reviewer for this important suggestion and have added a virtual channel analysis. We were however, not interested in alpha power in primary auditory cortex, as we were specifically interested in the posterior alpha, which is usually increased when expecting an auditory compared to a visual target (and used to be interpreted as a blanket inhibition of the visual cortex). We have now improved upon the clarity concerning this point in the manuscript.

We have however, followed the reviewer’s suggestion of a virtual channel analysis, showing that the condition differences are not observable in primary visual cortex for the 36 Hz visual signal and in primary auditory cortex for the 40 Hz auditory signal. Our data clearly shows that there is an alpha condition difference in V1, while there no condition difference for 36 Hz in V1 and for 40 Hz in Heschl’s Gyrus.

Line 356: Additionally, we replicated this effect with a virtual channel analysis in V1 (see SUPPL Fig. 12)

Line 403: Furthermore, a virtual channel analysis in V1 and Heschl’s gyrus confirmed that there were no condition differences in primary visual and auditory areas (see SUPPL Fig. 12).

(5) Blinking would have a huge impact on the subject's ability to ignore the visual distractor. The best thing to do would be to exclude from analysis all trials where the subjects blinked during the cue-to-target interval. The authors mention that in the MEG experiment, "To remove blinks, trials with very large eye-movements (> 10 degrees of visual angle) were removed from the data (See supplement Fig. 5)." This sentence needs to be clarified, since eye-movements cannot be measured during blinking. In addition, it seems possible to remove putative blink trials from EEG experiments as well, since blinks can be detected in the EEG signals.

We agree with the reviewer that this point has been phrased in a confusing way. From the MEG-data, we removed eyeblinks using ICA. Along for the supplementary Fig. 5 analysis, we used the eye-tracking data to make sure that participants were in fact fixating the centre of the screen. For this analysis, we removed trials with blinks (which can be seen in the eye-tracker as huge amplitude movements or as large eye-movements in degrees of visual angle; see figure below to show a blink in the MEG data and the according eye-tracker data in degrees of visual angle). We have now clarified this in the methods section.

As for the concern closed eyes to ignore visual distractors, in both experiments we can observe highly significant distractor cost in accuracy for visual distractors, which we hope will convince the reviewer that our visual distractors were working as intended.

Author response image 1.

Illustration of eye-tracker data for a trial without and a trial with a blink. All data points recorded during this trial are plottet. A, ICA component 1, which reflects blinks and its according data trace in a trial. No blink is visible. B, eye-tracker data transformed into degrees of visual angle for the trial depicted in A. C, ICA component 1, which reflects blinks and its according data trace in a trial. A clear blink is visible. D, eye-tracker data transformed into degrees of visual angle for the trial depicted in C.

Line 676: To confirm that participants had focused on the fixation cross during the cue-to-target interval, we incorporated eye-tracking into our MEG-experiment (EyeLink 1000 Plus). Correct trials of the second block were analysed for vertical and horizontal eye-movements. To exclude blinks from this analysis, trials with very large eye-movements (> 10 degrees of visual angle) were removed from the eye-tracking data (See suppl Fig. 5).

(6) It would be interesting to examine the neutral cue trials in this task. For example, comparing auditory vs visual vs neutral cue conditions would be indicative of whether alpha was actively recruited or actively suppressed. In addition, comparing spectral activity during cue-to-target period on neutral-cue auditory correct vs incorrect trials should mimic the comparison of auditory-cue vs visual-cue trials. Likewise, neutral-cue visual correct vs incorrect trials should mimic the attention-related differences in visual-cue vs auditory-cue trials.

We have analysed the neutral cue trials in the EEG dataset (see suppl. Fig. 1). There were no significant differences to auditory or visual cues, but descriptively alpha power was higher for neutral cues compared to visual cues and lower for neutral cues compared to auditory cues. While this may suggest that for visual trials alpha is actively suppressed and for auditory trials actively recruited, we do not feel comfortable to make this claim, as the neutral condition may not reflect a completely neutral state. The neutral task can still be difficult, especially because of the uncertainty of the target modality.

As for the analysis of incorrect versus correct trials, we appreciate the idea, but unfortunately the accuracy rate was quite high so that the number of incorrect trials is insufficient to perform a reliable analysis.

(7) In the abstract, the authors state that "This implies that alpha modulation does not solely regulate 'gain control' in early sensory areas but rather orchestrates signal transmission to later stages of the processing stream." However, I don't see any supporting evidence for the latter claim, that alpha orchestrates signal transmission to later stages of the processing stream. If the authors are claiming an alternative function to alpha, this claim should be strongly substantiated.

We thank the reviewer for pointing out, that we have not sufficiently explained our case. The first point refers to gain control as elucidated by the alpha inhibition hypothesis, which claims that increases in alpha disengage an entire cortical area. Since we have confirmed the alpha increase in our data to originate from primary visual cortex through source analysis, this should lead to decreased visual processing. The increase in 36 Hz visual processing therefore directly contradicts the alpha inhibition hypothesis. We propose an alternative explanation for the functionality of alpha activity in this task. Through pulsed inhibition, information packages of relevant visual information could be transmitted down the processing stream, thereby enhancing relevant visual signal transmission. We argue the fact that the enhanced visual 36 Hz signal we found correlated with visual alpha power on a trial-by-trial basis, and did not originate from primary visual cortex, but from areas known for sensory integration supports our claim.

We have now tried to make this point clearer by rephrasing our manuscript. Additionally, we have also now further clarified this point in our discussion.

Line 527: Our data provides evidence in favour of this view, as we can show that early sensory alpha activity covaries over trials with SSEP magnitude in higher order sensory areas. If alpha activity exerted gain control in early visual regions, increased alpha activity would have to lead to a decrease in SSEP responses. In contrast, we observe that increased alpha activity originating from early visual cortex is related to enhanced visual processing. Source localization confirmed that this enhancement was not originating from early visual areas, but from areas associated with later stages of the processing stream such as the precuneus, which has been connected to sensory integration (Al-Ramadhani et al., 2021; Xie et al., 2019). While we cannot completely rule out alternative explanations, it seems plausible to assume that inhibition of other task-irrelevant communication pathways leads to prioritised and thereby enhanced processing over relevant pathways. In line with previous literature (Morrow et al., 2023; Peylo et al., 2021; Zhigalov & Jensen, 2020b), we therefore suggest that alpha activity limits task-irrelevant feedforward communication, thereby enhancing processing capabilities in relevant downstream areas (see Fig. 1A).

Reviewer #1 (Recommendations for the authors):Minor Concerns:

(1) I suggest adding more details about the task in the Results and/or Figure 1 legend. Specifically, when describing the task, I think it would help the readers if the authors specified what the participants had to do to get a trial correct (e.g., press left / down / right arrow if the tone pitch was low (500Hz) / medium (1000Hz) / high (2000Hz).)

(2) Please clarify whether Gaboar patch was drifting.

(3) Figure 2C-D: I suggest clarifying in the X-tick labels that + and - trials are in separate blocks (e.g., put 'Block1 visual-' instead of 'visual-').

We followed the suggestions of the reviewer detailed in point 1-3, which indeed greatly improves the clarity and readability of these parts.

(4) "Interestingly, auditory distractors reduced reaction times to visual targets, which could be explained by a generally faster processing of auditory targets (Jain et al., 2015), possibly probing faster responses in visual tasks (Naue et al., 2011)." - Please elaborate on how faster processing of auditory targets could lead to the probing of faster responses in visual tasks. Further, if I understand correctly, this should result in a speed-accuracy trade-off, which is not observed in the MEG experiments. If there is a learning effect due to the blocked structure in the MEG experiments, why is it not observed on auditory trials?

We thank the reviewer for suggesting clarifying this paragraph. We have now rephrased this part and added additional information.

Concerning the reviewer’s theory, intersensory facilitation can occur in the absence of a speed-accuracy trade-off, as it can affect the motor execution after a decision has been made. Nevertheless, learning effects could also have led to this result in the MEG experiment. Our difficulty calibration did not lead to comparable accuracies in block 1, where auditory targets wetre now less difficult than visual targets. Whith the addition of distractors in block 2, accuracy for auditory targets decreased, while it increased for visual targets. Indeed, one interpretation could be that there was a learning effect for visual targets, which was not prevalent for auditory targets. However, the speed increase when visual targets are coupled with auditory distractors is prevalent in both experiments. Accordingly, we find the intersensory facilitation account more likely.

line 148: Interestingly, auditory distractors reduced reaction times to visual targets, which could be explained by a generally faster processing of auditory targets (Jain et al., 2015). As such, the auditory distractor possibly caused intersensory facilitation (Nickerson., 1973), whereby reaction times to a target can be facilitated when accompanied by stimuli of other sensory modalities, even if they are irrelevant or distracting.

(5) Please briefly describe the cluster permutation analysis in the results section.

We have now added a brief description of the cluster permutation analysis we performed in the results section.

Line 166: We then applied cluster permutation analysis, whereby real condition differences were tested against coincidental findings by randomly permutating the condition labels to the data and testing for condition differences 1000 times (Maris & Oostenveld, 2007).

(6) Figure 4A legend: "auditory steady-state evoked potential (ASSEP) averaged over 6 central electrodes displaying the highest 40 Hz power (Fz, FC1, FC2, F11, F2, FCz)." - I suggest marking these 6 electrodes in the scalp map on the figure panel.

We have followed the suggestion of the reviewer and marked the electrodes/sensors used to illustrate the steady-state responses.

(7) Lines 281-283: "It was highly significant for the visual 36 Hz response (Fig. 5A, middle columns, p = .033; t(19) = 2.29; BF(10) = 1.91) but did not reach significance for the visual 40 Hz response (Fig. 5B, middle column; p = 0.20; t(19) = 1.32; BF(10) = 0.49)." - Was "visual 40Hz response" a typo? I believe 40Hz pertains to auditory, not visual?

We thank the reviewer for pointing out this error and agree that the phrasing was sometimes confusing. We have now used the terms VSSEP and ASSEP to make things clearer throughout the manuscript.

L. 224-229: The median split was highly significant for the 36 Hz VSSEP response (Fig. 5A, middle columns, p \= .033; t₍₁₉₎ = 2.29; BF₍₁₀₎ = 1.91) but did not reach significance for the 40 Hz ASSEP response (Fig. 5B, middle column; p = 0.20; t₍₁₉₎ = 1.32; BF₍₁₀₎ = 0.49).

Reviewer #2 (Public review):

Brickwedde et al. investigate the role of alpha oscillations in allocating intermodal attention. A first EEG study is followed up with an MEG study that largely replicates the pattern of results (with small to be expected differences). They conclude that a brief increase in the amplitude of auditory and visual stimulus-driven continuous (steady-state) brain responses prior to the presentation of an auditory - but not visual - target speaks to the modulating role of alpha that leads them to revise a prevalent model of gating-by-inhibition.

Overall, this is an interesting study on a timely question, conducted with methods and analysis that are state-of-the-art. I am particularly impressed by the author's decision to replicate the earlier EEG experiment in MEG following the reviewer's comments on the original submission. Evidently, great care was taken to accommodate the reviewers suggestions.

We thank the reviewer for the positive feedback and expression of interest in the topic of our manuscript.

Nevertheless, I am struggling with the report for two main reasons: It is difficult to follow the rationale of the study, due to structural issues with the narrative and missing information or justifications for design and analysis decisions, and I am not convinced that the evidence is strong, or even relevant enough for revising the mentioned alpha inhibition theory. Both points are detailed further below.

We have now revised major parts of the introduction and results in line with the reviewer’s suggestions, hoping that our rationale is now easier to follow and that our evidence will now be more convincing. We have separated our results section into the first study (EEG) and to second study (MEG), to enhance the rationale of our design choices and readability. We have clarified all mentioned ambiguous parts in our methods section. Additionally, we have revised the introduction to now explain more clearly what results to expect under the alpha inhibition theory in contrast to our alternative account.

Strength/relevance of evidence for model revision: The main argument rests on 1) a rather sustained alpha effect following the modality cue, 2) a rather transient effect on steady-state responses just before the expected presentation of a stimulus, and 3) a correlation between those two. Wouldn't the authors expect a sustained effect on sensory processing, as measured by steady-state amplitude irrespective of which of the scenarios described in Figure 1A (original vs revised alpha inhibition theory) applies? Also, doesn't this speak to the role of expectation effects due to consistent stimulus timing? An alternative explanation for the results may look like this: Modality-general increased steady-state responses prior to the expected audio stimulus onset are due to increased attention/vigilance. This effect may be exclusive (or more pronounced) in the attend-audio condition due to higher precision in temporal processing in the auditory sense or, vice versa, too smeared in time due to the inferior temporal resolution of visual processing for the attend-vision condition to be picked up consistently. As expectation effects will build up over the course of the experiment, i.e., while the participant is learning about the consistent stimulus timing, the correlation with alpha power may then be explained by a similar but potentially unrelated increase in alpha power over time.

We thank the reviewer for raising these insightful questions and suggestions.

It is true that our argument rests on a rather sustained alpha effect and a rather transient effect on steady-state responses ,and a correlation between the two. However, this connection would not be expected under the alpha inhibition hypothesis, which states that alpha activity would inhibit a whole cortical area (when irrelevant to the task), exerting “gain control”. This notion directly contradicts our results of the “irrelevant” visual information a) being transmitted at all and b) increasing.

However, it has been shown in various reports (see for instance Dugué et al., 2011; Haegens et al., 2011; Spaak et al., 2012) that alpha activity exerts pulsed inhibition, so we proposed an alternative theory of an involvement in signal transmission. In this case, the cyclic inhibition would serve as an ordering system, which only allows for high-priority information to pass, resulting in higher signal-to-noise ratio. We do not make a claim about how fast or when these signals are transmitted in relation to alpha power. For instance, it could be that alpha power increases as a preparatory state even before signal is actually transmitted.  Zhigalov (2020 Hum. Brain M.) has shown that in V1, frequency-tagging responses were up-and down regulated with attention – independent of alpha activity.

However, we do believe that visual alpha power correlates on a trial-by-trial level with visual 36 Hz frequency-tagging increases (see Fig. 5 and 10 in our manuscript) - a relationship which has not been found in V1 by us and others (see SUPPL Fig. 12 and Zhigalov 2020, Hum. Brain Mapp.) suggest a strong connection. Furthermore, the fact that the alpha modulation originates from early visual areas and occurs prior to any frequency-tagging changes, while the increase in frequency-tagging can be observed in areas which are later in the processing stream (such as the precuneus) is strongly indicative for an involvement of alpha power in the transmission of this signal. We cannot fully exclude alternative accounts and mechanisms which effect both alpha power and frequency-tagging responses.  

The alternative account described by the reviewer does not contradict our theory, as we argue that the alpha power modulation reflects an expectation effect (and the idea that it could be related to the resolution of auditory versus visual processing is very interesting!). It is also possible that this expectation is, as the reviewer suggests, related to attention/vigilance and might result in a modality-general signal increase. By way of support, we observed an increase in the frequency-tagging response in sensory integration areas. Accordingly, we argue that the alternative explanation provided by the reviewer contradicts the alpha inhibition hypothesis, but not necessarily our alternative theory.

We have now revised the discussion and are confident our case is now stronger and easier to follow. Additionally, we mentioned the possibility for alternative explanations as well as the possibility, that alpha networks fulfil different roles in different locations/task environments.

Line 523: Here we propose that alpha activity, rather than modulating early primary sensory processing, exhibits its inhibitory effects at later stages of the processing stream (Antonov et al., 2020; Gundlach et al., 2020; Zhigalov & Jensen, 2020a; Zumer et al., 2014), gating feedforward or feedback communication between sensory areas (Bauer et al., 2020; Haegens et al., 2015; Uemura et al., 2021). Our data provides evidence in favour of this view, as we can show that early sensory alpha activity covaries over trials with SSEP magnitude in higher order sensory areas. If alpha activity exerted gain control in early visual regions, increased alpha activity would have to lead to a decrease in SSEP responses. In contrast, we observe that increased alpha activity originating from early visual cortex is related to enhanced visual processing. Source localization confirmed that this enhancement was not originating from early visual areas, but from areas associated with later stages of the processing stream such as the precuneus, which has been connected to sensory integration (Al-Ramadhani et al., 2021; Xie et al., 2019). While we cannot completely rule out alternative explanations, it seems plausible to assume that inhibition of other task-irrelevant communication pathways leads to prioritised and thereby enhanced processing over relevant pathways. In line with previous literature (Morrow et al., 2023; Peylo et al., 2021; Zhigalov & Jensen, 2020b), we therefore suggest that alpha activity limits task-irrelevant feedforward communication, thereby enhancing processing capabilities in relevant downstream areas (see Fig. 1A).

References:

Dugué, L., Marque, P., & VanRullen, R. (2011). The phase of ongoing oscillations mediates the causal relation between brain excitation and visual perception. Journal of Neuroscience, 31(33), 11889–11893. https://doi.org/10.1523/JNEUROSCI.1161-11.2011

Haegens, S., Nácher, V., Luna, R., Romo, R., & Jensen, O. (2011). α-Oscillations in the monkey sensorimotor network influence discrimination performance by rhythmical inhibition of neuronal spiking. Proceedings of the National Academy of Sciences, 108(48), 19377–19382. https://doi.org/10.1073/PNAS.1117190108

Spaak, E., Bonnefond, M., Maier, A., Leopold, D. A., & Jensen, O. (2012). Layer-Specific Entrainment of Gamma-Band Neural Activity by the Alpha Rhythm in Monkey Visual Cortex. Current Biology, 22(24), 2313–2318. https://doi.org/10.1016/J.CUB.2012.10.020

Zhigalov, A., & Jensen, O. (2020). Alpha oscillations do not implement gain control in early visual cortex but rather gating in parieto-occipital regions. Human Brain Mapping, 41(18), 5176–5186. https://doi.org/10.1002/hbm.25183

Structural issues with the narrative and missing information: Here, I am mostly concerned with how this makes the research difficult to access for the reader. I list the some major, followed by more specific points below:

In the introduction the authors pit the original idea about alpha's role in gating against some recent contradictory results. If it's the aim of the study to provide evidence for either/or, predictions for the results from each perspective are missing. Also, it remains unclear how this relates to the distinction between original vs revised alpha inhibition theory (Fig. 1A). Relatedly, if this revision is an outcome rather than a postulation for this study, it shouldn't be featured in the first figure.

We agree with the reviewer that we have not sufficiently clarified our goal as well as how different functionalities of alpha oscillations would lead to different outcomes. We have revised the introduction and restructured the results part and hope that it is now easier to follow. The results part now follows study 1 (EEG) and study 2 (MEG) chronologically, so that results can more easily be differentiated and our design choices for the second study can be explained better.

Line 50: Recent evidence challenged a direct connection between alpha activity and visual information processing in early visual cortex. As such, both visual steady-state responses and alpha power were modulated by attention, but did not covary when investigating individual trials (Zhigalov & Jensen, 2020). Unfortunately, very few studies have investigated direct connections between alpha activity, attention and sensory signals, especially over trials. Furthermore, results seem to depend on timing of alpha activity in relation to sensory responses as well as stimulus type and outcome measure (Morrow et al., 2023).

Accordingly, the objective of the current study is to test the alpha inhibition hypothesis compared to an alternative theory. Based on the alpha inhibition hypothesis, alpha modulation is connected to ‘gain control’ in early visual areas through modulation of excitability (Foxe & Snyder, 2011; Jensen & Mazaheri, 2010; Van Diepen et al., 2019).  In contrast, we propose that inhibitory effects of alpha modulation are exhibited at later stages of the processing stream (Peylo et al., 2021; Yang et al., 2023; Zhigalov & Jensen, 2020a; Zumer et al., 2014), gating feedforward or feedback communication between sensory areas (see Fig. 1B; Bauer et al., 2020; Haegens et al., 2015; Uemura et al., 2021).

Line 80: The aim of our study was to directly test the alpha inhibition hypothesis by investigating if cue-induced modulation of alpha activity coincides with the suppression of frequency-tagging responses in task-irrelevant modalities.

Line 99: In brief, while we observed the expected cue-induced early-visual alpha modulation, the amplitude of auditory and visual SSEP/SSEFs as well as their intermodulation frequency increased just prior to the onset of the auditory target, contradicting the alpha inhibition hypothesis. The difference between conditions of visual SSEP/SSEFs originated from sensory integration areas and correlated with early sensory alpha activity on a trial-by-trial basis, speaking to an effect of alpha modulation on signal transmission rather than inhibition of early visual areas.

The analysis of the intermodulation frequency makes a surprise entrance at the end of the Results section without an introduction as to its relevance for the study. This is provided only in the discussion, but with reference to multisensory integration, whereas the main focus of the study is focussed attention on one sense. (Relatedly, the reference to "theta oscillations" in this sections seems unclear without a reference to the overlapping frequency range, and potentially more explanation.) Overall, if there's no immediate relevance to this analysis, I would suggest removing it.

We thank the reviewer for pointing this out and have now added information about this frequency to the introduction. We believe that the intermodulation frequency analysis is important, as it potentially supports the notion that condition differences in the visual-frequency tagging response are related to downstream processing rather than overall visual information processing in V1. We would therefore prefer to leave this analysis in the manuscript.

Line 75: Furthermore, when applying two different frequencies for two different sensory modalities, their intermodulation frequency (f1-f2) has been suggested to reflect cross-modal integration (Drijvers et al., 2021). Due to distinct responses, localisation and attention-dependence, frequency-tagging provides an optimal tool to study sensory signal processing and integration over time.

Reviewer #2 (Recommendations for the authors):

As detailed in several points below, I found that I didn't get the information I needed to fully understand design/analysis decisions. In some cases, this may just be a case of re-organising the manuscript, in others crucial info should be added:

Specific issues:

Page 2, line 51: How does recent evidence contradict this? Please explain.

We have added a section that describes the results contradicting the alpha inhibition hypothesis.

Line 50: Recent evidence challenged a direct connection between alpha activity and visual information processing in early visual cortex. As such, both visual steady-state responses and alpha power were modulated by attention, but did not covary when investigating individual trials (Zhigalov & Jensen, 2020).

Page 3, line 78-80: "... also interested in relationships [...] on a trial-by-trial basis" - why? Please motivate.

We thank the reviewer for highlighting this section, which we feel was not very well phrased. We have rewritten this whole paragraph and hope that our motivation for this study is now clear.

Line 50: Recent evidence challenged a direct connection between alpha activity and visual information processing in early visual cortex. As such, both visual steady-state responses and alpha power were modulated by attention, but did not covary when investigating individual trials (Zhigalov & Jensen, 2020). Unfortunately, very few studies have investigated direct connections between alpha activity, attention and sensory signals, especially over trials. Furthermore, results seem to depend on timing of alpha activity in relation to sensory responses as well as stimulus type and outcome measure (Morrow et al., 2023).

Page 4, line 88-92: "... implementing a blocked design" - unclear why? This is explained to some extent in the next few lines but remains unclear without knowing outcomes of the EEG experiment with more detail. Overall, it seems like this methodological detail may be better suited for a narrative in the Results section, that follows a more chronological order from the findings of the EEG experiment to the design of the MEG study.

More generally, and maybe I missed it, I couldn't find a full account of why a block design was chosen and what the added value was. I believe that re-organising the Results section would allow precisely stating how that was an improvement over the EEG experiment.

In line with the reviewer’s suggestion, we have now restructured the results section. The first section of the study 2 results now explains our design choices with direct reference to the results of the EEG experiment.

Line 298: To test the robustness of our results and to employ additional control analyses, we replicated our experiment using MEG (see Fig. 7A). While an increase in visual information processing parallel to an increase in alpha modulation already contradicts the notion of alpha inhibition exerting “gain control”, affecting the whole visual cortex, our claim that alpha modulation instead affects visual information at later processing stages still required further validation. As such, our goal was to perform source analyses showing alpha modulation originating from primary visual areas affected visual information at later processing stages (e.g. not in primary visual cortex). Additionally, to exclude that the uncertainty over possible distractors affected our results, we employed a block design, where block 1 consisted only of trials without distractors and in block 2 targets were always accompanied by a distractor. Furthermore, we aligned the visual and auditory task to be more similar, both of them now featuring frequency-discrimination, which related to sound pitch (frequency) in the auditory condition and stripe-frequency of the Gabor patch in the visual condition. Lastly, to make sure our effects were driven by sensory modality-differences rather than task-difficulty differences, we included a short calibration phase. Prior to the experiment, difficulty of pitch sounds, and Gabor patch frequency were calibrated for each individual, ascertaining a success rate between 55% to 75%.

The point above also applies to lines 95-97 where it's unclear what "aligning the visual with the auditory task" means. Also, what would be the predictions for "more nuanced interactions [...]"

We agree that this phrasing was more than confusing and in the process of restructuring our results section, we have now revised this passage (see cited text from our manuscript to the point just above).

Page 9, line 207-209: One of the few mentions of the "ambivalent" condition (attention to audio+vision?). To what end was that condition added to the experiment originally? The explanation that this condition was dropped from analysis because it did not show significant results does not seem methodologically sound.

We thank the reviewer for pointing this out, as we had changed the name from ambivalent to non-specific, but this word had slipped our attention. The condition was added to the experiment as a control, which enables us to verify that our cues as well as our distractors work as intended. While interesting to analyse (and we did not drop it completely, the condition comparisons are in the supplementary material), we felt that further analysis of this condition would not contribute to addressing our research question. To be specific, the prerequisite to analysing the effect of alpha modulation is a significant effect of alpha modulation in the first place. We have now clarified the rationale for this condition, as well as our reasoning for omitting it from correlation and source analysis.

Line 173 When presenting unspecified cues, alpha power changes were not significant, but descriptively larger compared to visual target conditions and lower compared to auditory target conditions (see suppl Fig. 2). However as significant alpha modulation was a prerequisite to test our hypotheses, we excluded this condition from further analysis.

Page 9, line 209-212: "condition differences in alpha were only significant in block 2 [...] therefore we performed the [...] analysis [...] only for the second half of the experiment." This sounds like double-dipping. Maybe just an issue of phrasing?

We thank the reviewer for pointing out that it may appear like ‘double dipping’. The reasoning was the same as the point above, we require a significant alpha modulation to test the effect of alpha modulation on further processing. We have revised this part to be clearer.

Line 345: In line with previous studies (van Diepen & Mazaheri, 2017), condition differences in alpha activity were only significant in block 2, where distractors were present. As alpha modulation was a prerequisite to test our hypotheses, we performed the following analyses solely with data from block 2 (see Fig. 8).

Page 12, line 281: Bayes factors are used here (and elsewhere), in addition to NHST. May be worthwhile to mention that briefly before use and give an intro sentence on its use, value and interpretation, and why these are added sometimes but not for all tests reported.

We agree that we did not introduce this at all and have now added a section, which explains the inclusion as well as the interpretation of the Bayes factor.

Line 218: To estimate the robustness of these results, we additionally conducted median split analyses between trials with high and low alpha power for each participant, as well as averaged the correlation coefficient of each participant and calculated a one-sample t-test against 0. For each analysis we provided the Bayes Factor, which estimates the strength of support for or against the null hypothesis (BF > 3.2 is considered as substantial evidence and BF > 10 is considered as strong evidence; Kass & Raftery, 1995).

Throughout the Results section, it's not always clear which results are from the EEG or from the MEG study. Adopting the recommendation in point c) may help with that.

According to the reviewer’s recommendation, we have restructured our results section and first present the EEG study and afterwards the MEG study.

Similarly, it seems pivotal to add "visual" and "auditory" when mentioning the 36/40-Hz steady-state responses (or stimulation) to help the reader.

We agree that visual/auditory 36 Hz / 40 Hz frequency-tagging responses, expecting visual/auditory target becomes lengthy and confusing very quickly. We therefore decided to introduce the abbreviation of visual steady-state evoked potentials/fields (VSSEP/VSSEF) and auditory steady-state evoked potentials/fields (ASSEP/ASSEF).

Figure 5 - showing the same cluster as "early" and "late" in the margin for the MEG data is potentially confusing.

We thank the reviewer for pointing this out and have now adapted the figure to just show one cluster, as we only found this one cluster in our MEG analysis.

Reviewer #3 (Public review):

This paper seems very strong, particularly given that the follow-up MEG study both (a) clarifies the task design and separates the effect of distractor stimuli into other experimental blocks, and (b) provides source-localization data to more concretely address whether alpha inhibition is occurring at or after the level of sensory processing, and (c) replicates most of the EEG study's key findings.

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

There are some points that would be helpful to address to bolster the paper. First, the introduction would benefit from a somewhat deeper review of the literature, not just reviewing when the effects of alpha seem to occur, but also addressing how the effect can change depending on task and stimulus design (see review by Morrow, Elias & Samaha (2023).

We thank the reviewer for this suggestion and agree. We have now added a paragraph to the introduction that refers to missing correlation studies and the impact of task design.

Line 53: Unfortunately, very few studies have investigated direct connections between alpha activity, attention and sensory signals, especially over trials. Furthermore, results seem to depend on timing of alpha activity in relation to sensory responses as well as stimulus type and outcome measure (Morrow et al., 2023).

Additionally, the discussion could benefit from more cautionary language around the revision of the alpha inhibition account. For example, it would be helpful to address some of the possible discrepancies between alpha and SSEP measures in terms of temporal specificity, SNR, etc. (see Peylo, Hilla, & Sauseng, 2021). The authors do a good job speculating as to why they found differing results from previous cross-modal attention studies, but I'm also curious whether the authors think that alpha inhibition/modulation of sensory signals would have been different had the distractors been within the same modality or whether the cues indicated target location, rather than just modality, as has been the case in so much prior work?

We thank the reviewer for suggesting these interesting discussion points and have included a paragraph in our discussion that clarifies these issues.

Line 543: It should be noted, the comparison between modulation in alpha activity and in SSEP/SSEFs is difficult, especially concerning timing. This is largely owed to differences in signal-to-noise due to trial averaging in the frequency versus the time domain and temporal and frequency lag in the estimation of alpha activity (Peylo et al., 2021). It is further noteworthy, that the majority of evidence for the alpha inhibition hypothesis focused on the effect of pre-target alpha modulation on behaviour and target-related potentials (Morrow et al., 2023). However, in our data alpha modulation occurs clearly ahead of SSVEP/SSVEF modulation on a scale that could not be simply explained by temporal or frequency smearing. Additionally, significant trial-by-trial correlations, which occur in the frequency domain for both signal types, underline the strong relationship between both measurements.

Interestingly, we could show that the magnitude of the correlation between alpha power and visual information processing varied between conditions, suggesting a dynamic and adaptive regime. This notion supports the view that alpha oscillations represent a mechanism rather than a specific function, which can fulfil different roles depending on task demand and network location, which has been confirmed in a recent study revealing functionally distinct alpha networks (Clausner et al., 2024). As such, it is conceivable that alpha oscillations can in some cases inhibit local processing, while in other cases, depending on network location, connectivity and demand, alpha oscillation can facilitate signal transmission. In different contexts, utilizing unimodal targets and distractors, spatial cueing, or covert attention, different functional processes could be involved (Morrow et al., 2023). Future research should intensify efforts to disentangle these effects, investigating localized alpha networks intracranially or through combinations of fMRI, EEG and MEG, to clearly measure their effects on sensory processing and behaviour.

Overall, the analyses and discussion are quite comprehensive, and I believe this paper to be an excellent contribution to the alpha-inhibition literature.

Reviewer #3 (Recommendations for the authors):

Overall, the paper is well-written, and the analyses and interpretations are strong. I think that the end of the introduction would feel more complete and more read more easily if you outlined all of your main hypotheses (not just trials signaling an auditory stimulus, but visual trials too, and what about distractor trials? This could help justify changes to task design in the MEG study), and then the key findings that motivated the follow-up design, which you then discuss (as opposed to introducing a new aim in this paragraph).

We thank the reviewer for this positive evaluation. Based on feedback und suggestions from all reviewers, we have revised the structure of the manuscript. The introduction now states more clearly which results would be expected under the alpha inhibition theory and how our results contradict this. The results section has now been divided into two studies, which will make the rationale for our follow-up design easier to follow.

Line 80: The aim of our study was to directly test the alpha inhibition hypothesis by investigating if cue-induced modulation of alpha activity coincides with the suppression of frequency-tagging responses in task-irrelevant modalities.

Line 96: In brief, while we observed the expected cue-induced early-visual alpha modulation, the amplitude of auditory and visual SSEP/SSEFs as well as their intermodulation frequency increased just prior to the onset of the auditory target, contradicting the alpha inhibition hypothesis. The difference between conditions of visual SSEP/SSEFs originated from sensory integration areas and correlated with early sensory alpha activity on a trial-by-trial basis, speaking to an effect of alpha modulation on signal transmission rather than inhibition of early visual areas.

Minor issues:

L84 - "is" should be "was"

L93 - "allows" should be "allowed"

L113 - I think "changed" would suffice

Fig 1A (text within figure on top) - "erea" should be "area" and caption title should include "of" (Illustration of the...)

L213 - time window could be clarified

Fig 4 -captions inconsistently capitalize words and use ) and , following the caption letters

L253-255 - give you are looking at condition differences, do you mean the response was larger before an auditory target than before a visual target? It currently reads as if you mean that it was larger in that window right before the target as opposed to other time windows

L368 - "behaviorally" should be "behavioral"

L407-408 - I think auditory SSEP/SSVEFs should be auditory or visual SSEP/SSEFs, unless you are specifically only talking about auditory SSEPs and visual SSEFs

L411 - also uses SSVEFs

L413 - "frequently, or in the case of..."

L555 - "predicting" should be predicted? Or do you mean only cues that correctly predicted the target?

We are very grateful for the reviewer for pointing out these mistakes, all of which we have remedied in our manuscript.

Author Response

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

eLife assessment

This study presents potentially valuable results on glutamine-rich motifs in relation to protein expression and alternative genetic codes. The author's interpretation of the results is so far only supported by incomplete evidence, due to a lack of acknowledgment of alternative explanations, missing controls and statistical analysis and writing unclear to non experts in the field. These shortcomings could be at least partially overcome by additional experiments, thorough rewriting, or both.

We thank both the Reviewing Editor and Senior Editor for handling this manuscript.

Based on your suggestions, we have provided controls, performed statistical analysis, and rewrote our manuscript. The revised manuscript is significantly improved and more accessible to non-experts in the field.

Reviewer #1 (Public Review):

Summary

This work contains 3 sections. The first section describes how protein domains with SQ motifs can increase the abundance of a lacZ reporter in yeast. The authors call this phenomenon autonomous protein expression-enhancing activity, and this finding is well supported. The authors show evidence that this increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance, and that this phenomenon is not affected by mutants in translational quality control. It was not completely clear whether the increased protein abundance is due to increased translation or to increased protein stability.

In section 2, the authors performed mutagenesis of three N-terminal domains to study how protein sequence changes protein stability and enzymatic activity of the fusions. These data are very interesting, but this section needs more interpretation. It is not clear if the effect is due to the number of S/T/Q/N amino acids or due to the number of phosphorylation sites.

In section 3, the authors undertake an extensive computational analysis of amino acid runs in 27 species. Many aspects of this section are fascinating to an expert reader. They identify regions with poly-X tracks. These data were not normalized correctly: I think that a null expectation for how often poly-X track occur should be built for each species based on the underlying prevalence of amino acids in that species. As a result, I believe that the claim is not well supported by the data.

Strengths

This work is about an interesting topic and contains stimulating bioinformatics analysis. The first two sections, where the authors investigate how S/T/Q/N abundance modulates protein expression level, is well supported by the data. The bioinformatics analysis of Q abundance in ciliate proteomes is fascinating. There are some ciliates that have repurposed stop codons to code for Q. The authors find that in these proteomes, Q-runs are greatly expanded. They offer interesting speculations on how this expansion might impact protein function.

Weakness

At this time, the manuscript is disorganized and difficult to read. An expert in the field, who will not be distracted by the disorganization, will find some very interesting results included. In particular, the order of the introduction does not match the rest of the paper.

In the first and second sections, where the authors investigate how S/T/Q/N abundance modulates protein expression levels, it is unclear if the effect is due to the number of phosphorylation sites or the number of S/T/Q/N residues.

There are three reasons why the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities:

First, we have reported previously that phosphorylation-defective Rad51-NTD (Rad51-3SA) and wild-type Rad51-NTD exhibit similar autonomous PEE activity. Mec1/Tel1-dependent phosphorylation of Rad51-NTD antagonizes the proteasomal degradation pathway, increasing the half-life of Rad51 from ∼30 min to ≥180 min (1). (page 1, lines 11-14)

Second, in our preprint manuscript, we have already shown that phosphorylation-defective Rad53-SCD1 (Rad51-SCD1-5STA) also exhibits autonomous PEE activity similar to that of wild-type Rad53-SCD (Figure 2D, Figure 4A and Figure 4C). We have highlighted this point in our revised manuscript (page 9, lines 19-21).

Third, as revealed by the results of Figure 4, it is the percentages, and not the numbers, of S/T/Q/N residues that are correlated with the PEE activities of Q-rich motifs.

The authors also do not discuss if the N-end rule for protein stability applies to the lacZ reporter or the fusion proteins.

The autonomous PEE function of S/T/Q-rich NTDs is unlikely to be relevant to the N-end rule. The N-end rule links the in vivo half-life of a protein to the identity of its N-terminal residues. In S. cerevisiae, the N-end rule operates as part of the ubiquitin system and comprises two pathways. First, the Arg/N-end rule pathway, involving a single N-terminal amidohydrolase Nta1, mediates deamidation of N-terminal asparagine (N) and glutamine (Q) into aspartate (D) and glutamate (E), which in turn are arginylated by a single Ate1 R-transferase, generating the Arg/N degron. N-terminal R and other primary degrons are recognized by a single N-recognin Ubr1 in concert with ubiquitin-conjugating Ubc2/Rad6. Ubr1 can also recognize several other N-terminal residues, including lysine (K), histidine (H), phenylalanine (F), tryptophan (W), leucine (L) and isoleucine (I) (68-70). Second, the Ac/N-end rule pathway targets proteins containing N-terminally acetylated (Ac) residues. Prior to acetylation, the first amino acid methionine (M) is catalytically removed by Met-aminopeptidases (MetAPs), unless a residue at position 2 is non-permissive (too large) for MetAPs. If a retained N-terminal M or otherwise a valine (V), cysteine (C), alanine (A), serine (S) or threonine (T) residue is followed by residues that allow N-terminal acetylation, the proteins containing these AcN degrons are targeted for ubiquitylation and proteasome-mediated degradation by the Doa10 E3 ligase (71).

The PEE activities of these S/T/Q-rich domains are unlikely to arise from counteracting the N-end rule for two reasons. First, the first two amino acid residues of Rad51-NTD, Hop1-SCD, Rad53-SCD1, Sup35-PND, Rad51-ΔN, and LacZ-NVH are MS, ME, ME, MS, ME, and MI, respectively, where M is methionine, S is serine, E is glutamic acid and I is isoleucine. Second, Sml1-NTD behaves similarly to these N-terminal fusion tags, despite its methionine and glutamine (MQ) amino acid signature at the N-terminus. (Page 12, line 3 to page 13, line 2)

The most interesting part of the paper is an exploration of S/T/Q/N-rich regions and other repetitive AA runs in 27 proteomes, particularly ciliates. However, this analysis is missing a critical control that makes it nearly impossible to evaluate the importance of the findings. The authors find the abundance of different amino acid runs in various proteomes. They also report the background abundance of each amino acid. They do not use this background abundance to normalize the runs of amino acids to create a null expectation from each proteome. For example, it has been clear for some time (Ruff, 2017; Ruff et al., 2016) that Drosophila contains a very high background of Q's in the proteome and it is necessary to control for this background abundance when finding runs of Q's.

We apologize for not explaining sufficiently well the topic eliciting this reviewer’s concern in our preprint manuscript. In the second paragraph of page 14, we cite six references to highlight that SCDs are overrepresented in yeast and human proteins involved in several biological processes (5, 43) and that polyX prevalence differs among species (79-82).

We will cite a reference by Kiersten M. Ruff in our revised manuscript (38).

K. M. Ruff, J. B. Warner, A. Posey and P. S. Tan (2017) Polyglutamine length dependent structural properties and phase behavior of huntingtin exon1. Biophysical Journal 112, 511a.

The authors could easily address this problem with the data and analysis they have already collected. However, at this time, without this normalization, I am hesitant to trust the lists of proteins with long runs of amino acid and the ensuing GO enrichment analysis. Ruff KM. 2017. Washington University in St.

Ruff KM, Holehouse AS, Richardson MGO, Pappu RV. 2016. Proteomic and Biophysical Analysis of Polar Tracts. Biophys J 110:556a.

We thank Reviewer #1 for this helpful suggestion and now address this issue by means of a different approach described below.

Based on a previous study (43), we applied seven different thresholds to seek both short and long, as well as pure and impure, polyX strings in 20 different representative near-complete proteomes, including 4X (4/4), 5X (4/5-5/5), 6X (4/6-6/6), 7X (4/7-7/7), 8-10X (≥50%X), 11-10X (≥50%X) and ≥21X (≥50%X).

To normalize the runs of amino acids and create a null expectation from each proteome, we determined the ratios of the overall number of X residues for each of the seven polyX motifs relative to those in the entire proteome of each species, respectively. The results of four different polyX motifs are shown in our revised manuscript, i.e., polyQ (Figure 7), polyN (Figure 8), polyS (Figure 9) and polyT (Figure 10). Thus, polyX prevalence differs among species and the overall X contents of polyX motifs often but not always correlate with the X usage frequency in entire proteomes (43).

Most importantly, our results reveal that, compared to Stentor coeruleus or several non-ciliate eukaryotic organisms (e.g., Plasmodium falciparum, Caenorhabditis elegans, Danio rerio, Mus musculus and Homo sapiens), the five ciliates with reassigned TAAQ and TAGQ codons not only have higher Q usage frequencies, but also more polyQ motifs in their proteomes (Figure 7). In contrast, polyQ motifs prevail in Candida albicans, Candida tropicalis, Dictyostelium discoideum, Chlamydomonas reinhardtii, Drosophila melanogaster and Aedes aegypti, though the Q usage frequencies in their entire proteomes are not significantly higher than those of other eukaryotes (Figure 1). Due to their higher N usage frequencies, Dictyostelium discoideum, Plasmodium falciparum and Pseudocohnilembus persalinus have more polyN motifs than the other 23 eukaryotes we examined here (Figure 8). Generally speaking, all 26 eukaryotes we assessed have similar S usage frequencies and percentages of S contents in polyS motifs (Figure 9). Among these 26 eukaryotes, Dictyostelium discoideum possesses many more polyT motifs, though its T usage frequency is similar to that of the other 25 eukaryotes (Figure 10).

In conclusion, these new normalized results confirm that the reassignment of stop codons to Q indeed results in both higher Q usage frequencies and more polyQ motifs in ciliates.  

Reviewer #2 (Public Review):

Summary:

This study seeks to understand the connection between protein sequence and function in disordered regions enriched in polar amino acids (specifically Q, N, S and T). While the authors suggest that specific motifs facilitate protein-enhancing activities, their findings are correlative, and the evidence is incomplete. Similarly, the authors propose that the re-assignment of stop codons to glutamine-encoding codons underlies the greater user of glutamine in a subset of ciliates, but again, the conclusions here are, at best, correlative. The authors perform extensive bioinformatic analysis, with detailed (albeit somewhat ad hoc) discussion on a number of proteins. Overall, the results presented here are interesting, but are unable to exclude competing hypotheses.

Strengths:

Following up on previous work, the authors wish to uncover a mechanism associated with poly-Q and SCD motifs explaining proposed protein expression-enhancing activities. They note that these motifs often occur IDRs and hypothesize that structural plasticity could be capitalized upon as a mechanism of diversification in evolution. To investigate this further, they employ bioinformatics to investigate the sequence features of proteomes of 27 eukaryotes. They deepen their sequence space exploration uncovering sub-phylum-specific features associated with species in which a stop-codon substitution has occurred. The authors propose this stop-codon substitution underlies an expansion of ploy-Q repeats and increased glutamine distribution.

Weaknesses:

The preprint provides extensive, detailed, and entirely unnecessary background information throughout, hampering reading and making it difficult to understand the ideas being proposed.

The introduction provides a large amount of detailed background that appears entirely irrelevant for the paper. Many places detailed discussions on specific proteins that are likely of interest to the authors occur, yet without context, this does not enhance the paper for the reader.

The paper uses many unnecessary, new, or redefined acronyms which makes reading difficult. As examples:

1) Prion forming domains (PFDs). Do the authors mean prion-like domains (PLDs), an established term with an empirical definition from the PLAAC algorithm? If yes, they should say this. If not, they must define what a prion-forming domain is formally.

The N-terminal domain (1-123 amino acids) of S. cerevisiae Sup35 was already referred to as a “prion forming domain (PFD)” in 2006 (48). Since then, PFD has also been employed as an acronym in other yeast prion papers (Cox, B.S. et al. 2007; Toombs, T. et al. 2011).

B. S. Cox, L. Byrne, M. F., Tuite, Protein Stability. Prion 1, 170-178 (2007). J. A. Toombs, N. M. Liss, K. R. Cobble, Z. Ben-Musa, E. D. Ross, [PSI+] maintenance is dependent on the composition, not primary sequence, of the oligopeptide repeat domain. PLoS One 6, e21953 (2011).

2) SCD is already an acronym in the IDP field (meaning sequence charge decoration) - the authors should avoid this as their chosen acronym for Serine(S) / threonine (T)-glutamine (Q) cluster domains. Moreover, do we really need another acronym here (we do not).

SCD was first used in 2005 as an acronym for the Serine (S)/threonine (T)-glutamine (Q) cluster domain in the DNA damage checkpoint field (4). Almost a decade later, SCD became an acronym for “sequence charge decoration” (Sawle, L. et al. 2015; Firman, T. et al. 2018).

L. Sawle and K, Ghosh, A theoretical method to compute sequence dependent configurational properties in charged polymers and proteins. J. Chem Phys. 143, 085101(2015).

T. Firman and Ghosh, K. Sequence charge decoration dictates coil-globule transition in intrinsically disordered proteins. J. Chem Phys. 148, 123305 (2018).

3) Protein expression-enhancing (PEE) - just say expression-enhancing, there is no need for an acronym here.

Thank you. Since we have shown that the addition of Q-rich motifs to LacZ affects protein expression rather than transcription, we think it is better to use the “PEE” acronym.

The results suggest autonomous protein expression-enhancing activities of regions of multiple proteins containing Q-rich and SCD motifs. Their definition of expression-enhancing activities is vague and the evidence they provide to support the claim is weak. While their previous work may support their claim with more evidence, it should be explained in more detail. The assay they choose is a fusion reporter measuring beta-galactosidase activity and tracking expression levels. Given the presented data they have shown that they can drive the expression of their reporters and that beta gal remains active, in addition to the increase in expression of fusion reporter during the stress response. They have not detailed what their control and mock treatment is, which makes complete understanding of their experimental approach difficult. Furthermore, their nuclear localization signal on the tag could be influencing the degradation kinetics or sequestering the reporter, leading to its accumulation and the appearance of enhanced expression. Their evidence refuting ubiquitin-mediated degradation does not have a convincing control.

Although this reviewer’s concern regarding our use of a nuclear localization signal on the tag is understandable, we are confident that this signal does not bias our findings for two reasons. First, the negative control LacZ-NV also possesses the same nuclear localization signal (Figure 1A, lane 2). Second, another fusion target, Rad51-ΔN, does not harbor the NVH tag (Figure 1D, lanes 3-4). Compared to wild-type Rad51, Rad51-ΔN is highly labile. In our previous study, removal of the NTD from Rad51 reduced by ~97% the protein levels of corresponding Rad51-ΔN proteins relative to wild-type (1).

Based on the experimental results, the authors then go on to perform bioinformatic analysis of SCD proteins and polyX proteins. Unfortunately, there is no clear hypothesis for what is being tested; there is a vague sense of investigating polyX/SCD regions, but I did not find the connection between the first and section compelling (especially given polar-rich regions have been shown to engage in many different functions). As such, this bioinformatic analysis largely presents as many lists of percentages without any meaningful interpretation. The bioinformatics analysis lacks any kind of rigorous statistical tests, making it difficult to evaluate the conclusions drawn. The methods section is severely lacking. Specifically, many of the methods require the reader to read many other papers. While referencing prior work is of course, important, the authors should ensure the methods in this paper provide the details needed to allow a reader to evaluate the work being presented. As it stands, this is not the case.

Thank you. As described in detail below, we have now performed rigorous statistical testing using the GofuncR package (Figure 11, Figure 12 and DS7-DS32).

Overall, my major concern with this work is that the authors make two central claims in this paper (as per the Discussion). The authors claim that Q-rich motifs enhance protein expression. The implication here is that Q-rich motif IDRs are special, but this is not tested. As such, they cannot exclude the competing hypothesis ("N-terminal disordered regions enhance expression").

In fact, “N-terminal disordered regions enhance expression” exactly summarizes our hypothesis.

On pages 12-13 and Figure 4 of our preprint manuscript, we explained our hypothesis in the paragraph entitled “The relationship between PEE function, amino acid contents, and structural flexibility”.

The authors also do not explore the possibility that this effect is in part/entirely driven by mRNA-level effects (see Verma Na Comms 2019).

As pointed out by the first reviewer, we present evidence that the increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance (Figure 2), and that this phenomenon is not affected in translational quality control mutants (Figure 3).

As such, while these observations are interesting, they feel preliminary and, in my opinion, cannot be used to draw hard conclusions on how N-terminal IDR sequence features influence protein expression. This does not mean the authors are necessarily wrong, but from the data presented here, I do not believe strong conclusions can be drawn. That re-assignment of stop codons to Q increases proteome-wide Q usage. I was unable to understand what result led the authors to this conclusion.

My reading of the results is that a subset of ciliates has re-assigned UAA and UAG from the stop codon to Q. Those ciliates have more polyQ-containing proteins. However, they also have more polyN-containing proteins and proteins enriched in S/T-Q clusters. Surely if this were a stop-codon-dependent effect, we'd ONLY see an enhancement in Q-richness, not a corresponding enhancement in all polar-rich IDR frequencies? It seems the better working hypothesis is that free-floating climate proteomes are enriched in polar amino acids compared to sessile ciliates.

We thank this reviewer for raising this point, however her/his comments are not supported by the results in Figure 7.

Regardless, the absence of any kind of statistical analysis makes it hard to draw strong conclusions here.

We apologize for not explaining more clearly the results of Tables 5-7 in our preprint manuscript.

To address the concerns about our GO enrichment analysis by both reviewers, we have now performed rigorous statistical testing for SCD and polyQ protein overrepresentation using the GOfuncR package (https://bioconductor.org/packages/release/bioc/html/GOfuncR.html). GOfuncR is an R package program that conducts standard candidate vs. background enrichment analysis by means of the hypergeometric test. We then adjusted the raw p-values according to the Family-wise error rate (FWER). The same method had been applied to GO enrichment analysis of human genomes (89).

The results presented in Figure 11 and Figure 12 (DS7-DS32) support our hypothesis that Q-rich motifs prevail in proteins involved in specialized biological processes, including Saccharomyces cerevisiae RNA-mediated transposition, Candida albicans filamentous growth, peptidyl-glutamic acid modification in ciliates with reassigned stop codons (TAAQ and TAGQ), Tetrahymena thermophila xylan catabolism, Dictyostelium discoideum sexual reproduction, Plasmodium falciparum infection, as well as the nervous systems of Drosophila melanogaster, Mus musculus, and Homo sapiens (78). In contrast, peptidyl-glutamic acid modification and microtubule-based movement are not overrepresented with Q-rich proteins in Stentor coeruleus, a ciliate with standard stop codons.

Recommendations for the authors:

Please note that you control which revisions to undertake from the public reviews and recommendations for the authors.

Reviewer #1 (Recommendations For The Authors):

The order of paragraphs in the introduction was very difficult to follow. Each paragraph was clear and easy to understand, but the order of paragraphs did not make sense to this reader. The order of events in the abstract matches the order of events in the results section. However, the order of paragraphs in the introduction is completely different and this was very confusing. This disordered list of facts might make sense to an expert reader but makes it hard for a non-expert reader to understand.

Apologies. We endeavored to improve the flow of our revised manuscript to make it more readable.

The section beginning on pg 12 focused on figures 4 and 5 was very interesting and highly promising. However, it was initially hard for me to tell from the main text what the experiment was. Please add to the text an explanation of the experiment, because it is hard to figure out what was going on from the figures alone. Figure 4 is fantastic, but would be improved by adding error bars and scaling the x-axis to be the same in panels B,C,D.

Thank you for this recommendation. We have now scaled both the x-axis and y-axis equivalently in panels B, C and D of Figure 4. Error bars are too small to be included.

It is hard to tell if the key variable is the number of S/T/Q/N residues or the number of phosphosites. I think a good control would be to add a regression against the number of putative phosphosites. The sequences are well designed. I loved this part but as a reader, I need more interpretation about why it matters and how it explains the PEE.

As described above, we have shown that the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities.

I believe that the prevalence of polyX runs is not meaningful without normalizing for the background abundance of each amino acid. The proteome-wide abundance and the assumption that amino acids occur independently can be used to form a baseline expectation for which runs are longer than expected by chance. I think Figures 6 and 7 should go into the supplement and be replaced in the main text with a figure where Figure 6 is normalized by Figure 7. For example in P. falciparum, there are many N-runs (Figure 6), but the proteome has the highest fraction of N’s (Figure 7).

Thank you for these suggestions. The three figures in our preprint manuscript (Figures 6-8) have been moved into the supplementary information (Figures S1-S3). For normalization, we have provided four new figures (Figures 7-10) in our revised manuscript.

The analysis of ciliate proteomes was fascinating. I am particularly interested in the GO enrichment for “peptidyl-glutamic acid modification” (pg 20) because these enzymes might be modifying some of Q’s in the Q-runs. I might be wrong about this idea or confused about the chemistry. Do these ciliates live in Q-rich environments? Or nitrogen rich environments?

Polymeric modifications (polymodifications) are a hallmark of C-terminal tubulin tails, whereas secondary peptide chains of glutamic acids (polyglutamylation) and glycines (polyglycylation) are catalyzed from the γ-carboxyl group of primary chain glutamic acids. It is not clear if these enzymes can modify some of the Q’s in the Q-runs.

To our knowledge, ciliates are abundant in almost every liquid water environment, i.e., oceans/seas, marine sediments, lakes, ponds, and rivers, and even soils.

I think you should include more discussion about how the codons that code for Q’s are prone to slippage during DNA replication, and thus many Q-runs are unstable and expand (e.g. Huntington’s Disease). The end of pg 24 or pg 25 would be good places.

We thank the reviewer for these comments.

PolyQ motifs have a particular length-dependent codon usage that relates to strand slippage in CAG/CTG trinucleotide repeat regions during DNA replication. In most organisms having standard genetic codons, Q is encoded by CAGQ and CAAQ. Here, we have determined and compared proteome-wide Q contents, as well as the CAGQ usage frequencies (i.e., the ratio between CAGQ and the sum of CAGQ, CAGQ, TAAQ, and TAGQ).

Our results reveal that the likelihood of forming long CAG/CTG trinucleotide repeats are higher in five eukaryotes due to their higher CAGQ usage frequencies, including Drosophila melanogaster (86.6% Q), Danio rerio (74.0% Q), Mus musculus (74.0% Q), Homo sapiens (73.5% Q), and Chlamydomonas reinhardtii (87.3% Q) (orange background, Table 2). In contrast, another five eukaryotes that possess high numbers of polyQ motifs (i.e., Dictyostelium discoideum, Candida albicans, Candida tropicalis, Plasmodium falciparum and Stentor coeruleus) (Figure 1) utilize more CAAQ (96.2%, 84.6%, 84.5%, 86.7% and 75.7%) than CAAQ (3.8%, 15.4%, 15.5%, 13.3% and 24.3%), respectively, to avoid the formation of long CAG/CTG trinucleotide repeats (green background, Table 2). Similarly, all five ciliates with reassigned stop codons (TAAQ and TAGQ) have low CAGQ usage frequencies (i.e., from 3.8% Q in Pseudocohnilembus persalinus to 12.6% Q in Oxytricha trifallax) (red font, Table 2). Accordingly, the CAG-slippage mechanism might operate more frequently in Chlamydomonas reinhardtii, Drosophila melanogaster, Danio rerio, Mus musculus and Homo sapiens than in Dictyostelium discoideum, Candida albicans, Candida tropicalis, Plasmodium falciparum, Stentor coeruleus and the five ciliates with reassigned stop codons (TAAQ and TAGQ).

Author response table 1.

Usage frequencies of TAA, TAG, TAAQ, TAGQ, CAAQ and CAGQ codons in the entire proteomes of 20 different organisms.

Pg 7, paragraph 2 has no direction. Please add the conclusion of the paragraph to the first sentence.

This paragraph has been moved to the “Introduction” section” of the revised manuscript.

Pg 8, I suggest only mentioning the PFDs used in the experiments. The rest are distracting.

We have addressed this concern above.

Pg 12. Please revise the "The relationship...." text to explain the experiment.

We apologize for not explaining this topic sufficiently well in our preprint manuscript.

SCDs are often structurally flexible sequences (4) or even IDRs. Using IUPred2A (https://iupred2a.elte.hu/plot_new), a web-server for identifying disordered protein regions (88), we found that Rad51-NTD (1-66 a.a.) (1), Rad53-SCD1 (1-29 a.a.) and Sup35-NPD (1-39 a.a.) are highly structurally flexible. Since a high content of serine (S), threonine (T), glutamine (Q), asparanine (N) is a common feature of IDRs (17-20), we applied alanine scanning mutagenesis approach to reduce the percentages of S, T, Q or N in Rad51-NTD, Rad53-SCD1 or Sup35-NPD, respectively. As shown in Figure 4 and Figure 5, there is a very strong positive relationship between STQ and STQN amino acid percentages and β-galactosidase activities. (Page 13, lines 5-10)

Pg 13, first full paragraph, "Futionally, IDRs..." I think this paragraph belongs in the Discussion.

This paragraph is now in the “Introduction” section (Page 5, Lines 11-15).

Pg. 15, I think the order of paragraphs should be swapped.

These paragraphs have been removed or rewritten in the “Introduction section” of our revised manuscript.

Pg 17 (and other parts) I found the lists of numbers and percentages hard to read and I think you should refer readers to the tables.

Thank you. In the revised manuscript, we have avoided using lists of numbers and percentages, unless we feel they are absolutely essential.

Pg. 19 please add more interpretation to the last paragraph. It is very cool but I need help understanding the result. Are these proteins diverging rapidly? Perhaps this is a place to include the idea of codon slippage during DNA replication.

Thank you. The new results in Table 2 indicate that the CAG-slippage mechanism is unlikely to operate in ciliates with reassigned stop codons (TAAQ and TAGQ).

Pg 24. "Based on our findings from this study, we suggest that Q-rich motifs are useful toolkits for generating novel diversity during protein evolution, including by enabling greater protein expression, protein-protein interactions, posttranslational modifications, increased solubility, and tunable stability, among other important traits." This idea needs to be cited. Keith Dunker has written extensively about this idea as have others. Perhaps also discuss why Poly Q rich regions are different from other IDRs and different from other IDRs that phase-separate.

Agreed, we have cited two of Keith Dunker’s papers in our revised manuscript (73, 74).

Minor notes:

Please define Borg genomes (pg 25).

Borgs are long extrachromosomal DNA sequences in methane-oxidizing Methanoperedens archaea, which display the potential to augment methane oxidation (101). They are now described in our revised manuscript. (Page 15, lines 12-14)

Reviewer #2 (Recommendations For The Authors):

The authors dance around disorder but never really quantify or show data. This seems like a strange blindspot.

We apologize for not explaining this topic sufficiently well in our preprint manuscript. We have endeavored to do so in our revised manuscript.

The authors claim the expression enhancement is "autonomous," but they have not ruled things out that would make it not autonomous.

Evidence of the “autonomous” nature of expression enhancement is presented in Figure 1, Figure 4, and Figure 5 of the preprint manuscript.

Recommendations for improving the writing and presentation.

The title does not recapitulate the entire body of work. The first 5 figures are not represented by the title in any way, and indeed, I have serious misgivings as to whether the conclusion stated in the title is supported by the work. I would strongly suggest the authors change the title.

Figure 2 could be supplemental.

Thank you. We think it is important to keep Figure 2 in the text.

Figures 4 and 5 are not discussed much or particularly well.

This reviewer’s opinion of Figure 4 and Figure 5 is in stark contrast to those of the first reviewer.

The introduction, while very thorough, takes away from the main findings of the paper. It is more suited to a review and not a tailored set of minimal information necessary to set up the question and findings of the paper. The question that the authors are after is also not very clear.

Thank you. The entire “Introduction” section has been extensively rewritten in the revised manuscript.

Schematics of their fusion constructs and changes to the sequence would be nice, even if supplemental.

Schematics of the fusion constructs are provided in Figure 1A.

The methods section should be substantially expanded.

The method section in the revised manuscript has been rewritten and expanded. The six Javascript programs used in this work are listed in Table S4.

The text is not always suited to the general audience and readership of eLife.

We have now rewritten parts of our manuscript to make it more accessible to the broad readership of eLife.

In some cases, section headers really don't match what is presented, or there is no evidence to back the claim.

The section headers in the revised manuscript have been corrected.

A lot of the listed results in the back half of the paper could be a supplemental table, listing %s in a paragraph (several of them in a row) is never nice

Acknowledged. In the revised manuscript, we have removed almost all sentences listing %s.

Minor corrections to the text and figures.

There is a reference to table 1 multiple times, and it seems that there is a missing table. The current table 1 does not seem to be the same table referred to in some places throughout the text.

Apologies for this mistake, which we have now corrected in our revised manuscript.

In some places its not clear where new work is and where previous work is mentioned. It would help if the authors clearly stated "In previous work...."

Acknowledged. We have corrected this oversight in our revised manuscript.

Not all strains are listed in the strain table (KO's in figure 3 are not included)

Apologies, we have now corrected Table S2, as suggested by this reviewer.

Author response table 2.

S. cerevisiae strains used in this study

Author Response

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

On behalf of my co-authors, we thank you very much for giving us the opportunity to revise our manuscript entitled “A positive feedback loop between ZEB2 and ACSL4 regulates lipid metabolism to promote breast cancer metastasis” (manuscript number: eLife-RP-RA-2023-87510).

We would like to convey our appreciation to you and the expert reviewers for your valuable time and effort in reviewing and improving our work. We are grateful for the constructive comments raised by the six expert reviewers. We have studied the reviewer’s comments carefully and have accordingly conducted additional experiments as recommended. We have made the following revisions point by point. We found that our work was substantially strengthened by addressing these points.

Reviewer #1 (Public Review):

In this study, Jiamin Lin et al. investigated the potential positive feedback loop between ZEB2 and ACSL4, which regulates lipid metabolism and breast cancer metastasis. They reported a correlation between high expression of ZEB2 and ACSL4 and poor survival of breast cancer patients, and showed that depletion of ZEB2 or ACSL4 significantly reduced lipid droplets abundance and cell migration in vitro. The authors also claimed that ZEB2 activated ACSL4 expression by directly binding to its promoter, while ACSL4 in turn stabilized ZEB2 by blocking its ubiquitination. While the topic is interesting, there are several major concerns with the study and its conclusions are not convincing.

1) Figure 1A, the clinical relevance or biological significance of drug-resistant luminal breast cancer cell lines with metastatic cancer is questionable. Additionally, the RNA-seq analysis lacked multiple test correction for differential gene expression analysis, and no fold-change cut-off was used, leading to incorrect thresholds and wrongly identified significant signals.

We appreciate the reviewer’s valuable questions to improve our manuscript. We identified many EMT related transcription factors such as ZEB2, SNAIL, TWIST, etc. was up-regulated in drug-resistant cells, so we hypothesized that drug-resistant cells may undergone EMT and acquire metastatic capability. The drug-resistant cells used in this study had already been proved and examined in the previous studies of our research team as follows:

(1) Zheng FM, Long ZJ, Hou ZJ et al., A novel small molecule aurora kinase inhibitor attenuates breast tumor-initiating cells and overcomes drug resistance. Mol Cancer Ther. 2014 Aug;13(8):1991-2003.

(2) Yang N, Wang C, Wang Z, et al., FOXM1 recruits nuclear Aurora kinase A to participate in a positive feedback loop essential for the self-renewal of breast cancer stem cells. Oncogene. 2017 Jun 15;36(24):3428-3440.

For the second question, we used the fold-change cut-off in RNA-seq analysis and the fold change was over 1.5-fold and the adjust P value is less than 0.05. To make it more clearly, we have reset the cut off with a |log2FC|2 and p<0.05 and generated the volcano Plot using R4.3.0 software for differentially expressed genes as follows in Author response image 1. The results showed 3217 and 3035 up-regulated genes in TAXOL-resistant and EPI-resistant cells respectively, along with 2427 (TAXOL) and 2901 (EPI) down-regulated genes. Both ACSL4 and ZEB2 were up-regulated in two cell lines. We have put the figure in the new supplementary Fig S2.

Author response image 1.

2) Figure 1D-E, the clinical associations between ACSL4 and ZEB2 overexpression and poor patient survival are not justified. The authors used an old web tool, the Kaplan-Meier plotter database, based on microarray data, to perform the analysis. The reviewer repeated the analysis and found that multiple microarray probes for ZEB2 were available, leading to opposite results when different probes were selected. The reviewer also repeated the analysis using more reliable TCGA RNA-seq data and found no correlation between ASCL4 or ZEB2 expression and post-progression survival.

We appreciate the reviewer’s thoughtful questions. The Kaplan-Meier plotter database (http://kmplot.com/analysis/) we used is handled by a PostgreSQL server, which integrates gene expression and clinical data simultaneously including GEO, EGA and TCGA data. We used auto-select best cutoff for the the Kaplan-Meier analysis. Due to the web tool is old, we repeated the Kaplan-Meier survival analysis using R4.3.0 software and split the patients in TCGA database according to the third quartile expression (new Fig. 1D-F). The results also show that patients with high expression of ACSL4 and/or ZEB2 have relatively worse prognosis as follows in Author response image 2 (p<0.01):

Author response image 2.

3) Figure 1I relied on IHC to support the negative correlation between ACSL4 and Erα expression, but the small sample size limits the power to establish the relationship and the results are not definitive without further replication or biological investigation. The authors should provide more detailed and comprehensive analysis, including appropriate statistical tests, to ensure the findings are robust and reliable.

We appreciate the reviewer’s suggestion. To better understand the positive correlation between ACSL4 and ZEB2 expression, we add up to 45 breast cancer cases for IHC analysis and the correlation is shown as follows in Author response image 3 (new Fig. 1 H):

Author response image 3.

4) Figure 3B-C lacks justification of the differences by showing only one field without any internal control for exposure. The reviewer suggests to show additional fields where cells with both efficiently and inefficiently knocked-down are present, to justify the robustness of the results. This can also be achieved by mixing control and knockdown cells.

We totally understand the reviewer's concern. Thank you for pointing out this problem. The lower magnification field of view is shown as follows and it includes both efficiently and inefficiently knocked-down cells. We have changed the Fig. 3B and C as follows in Author response image 4:

Author response image 4.

5) Figure 4A-D, oleate-induced cell migration is a well-documented feature across different cancer types. To make it more relevant to the current study, the authors should examine multiple cell lines with high and low ZEB2/ACSL4 expression to determine the underlying relevance.

We appreciate the reviewer’s comments and performed the suggested experiments. To better determine the role of oleic acid and ACSL4 on cell migration, we use MCF-7 cell line, which has low ZEB2/ACSL4 expression, to test the influence of oleate on the cell migration. Transwell and Wound healing assays revealed that oleic acid treated MCF-7 cells also exhibited enhanced invasive and metastatic capacities compared with control cells. This results indicates that oleate induces cell migration in MCF-7 cells may via mechanisms other than ACSL4. We have added the results to the new Supplementary Fig. 8 as follows in Author response image 5.

Author response image 5.

6) Figure 4E, it is difficulty to conclude that cancer cells utilize stored lipids during migration to fuel metastasis based on current data. Do you see any evidence of lipid signal decreasing in the leading edge of the scratch wound-healing migration assay? The authors should also compare signals between unmigrated and migrated cells in the transwell assay.

We appreciate the reviewer’s constructive suggestion. We performed the wound-healing migration assay and observed that the lipid signal was obviously decreased in the leading edge of the scratch, as shown in the Author response image 6 (New Fig. 4E). In the transwell experiment, the cells which migrated to the lower side of the chamber after 24 hours showed decreased lipid signals (Fig. 4F). All these results indicates that lipid is utilized during migration.

Author response image 6.

7) Figure 6 warrants a genome-wide ChIP-seq to justify direct regulation of ASCL4 promoter by ZEB2. The reviewer’s analysis of publicly available ZEB2 ChIP-seq in multiple cell types detected no ZEB2 binding signaling within {plus minus} 5 kb of ASCL4 promoter.

We thank the reviewer for the concern. We found that the breast cancer cells are not included in some data base, such as Cistrome Data Browser, which is a resource of human and mouse cis-regulatory information derived from ChIP-seq, DNase-seq and ATAC-seq chromatin profiling assays. Due to that different cell type may have totally different mechanisms, that’s why the ZEB2 binding signaling cannot be found within ASCL4 promoter in some cells.

We searched JASPAR data base (https://jaspar.genereg.net/), which is an open-access database of non-redundant transcription factor (TF) binding profiles, and found the consensus binding sequences (CACCT) of ZEB (zinc finger E-box binding homeobox) transcription family were within the 2kb of ASCL4 promoter as follows in Author response image 7.

Author response image 7.

8) Figure 7 presents a series of self-contradictory results. Figure 7C, why no significant change in ZEB2-MYC expression was observed in the presence of ACSL4 and/or HA-Ubi? In Figure 7 E&G, why robust ACSL4 expression is present in the control group in E but not in (G)? Additionally, why there is no degradation in ZEB2 baseline level over time in the shACSL4 group in E? These raise severe concerns about the data quality.

We appreciate the reviewer to point out these problems.

Response to question 1: In fig. 7C, we used 293T cell for the ubiquitin assay and it is not a breast cancer cells. The efficiency of over-expression is different between ZEB2 and ACSL4 in 293T cell lines.

Response to question 2: Because the expression of ACSL4 is low in MCF-7 and is high in MDA-MB-231 cells. In Figure 7E (New Fig. 7G), we used MDA-MB-231 cells for the control and ACSL4 knockdown cells. In Figure 7G (New Fig. 7I), we used MCF-7 cells for the control and ACSL4 over-expressed cells. We have also revised the figure legend of Fig.7 as follows:

I, The stability of ZEB2 protein was detected by CHX treatment assay in control or ACSL4 over-expressed MCF-7 cells. GAPDH was used as the internal loading control.

Response to question 3: Because knockdown of ACSL4 also significantly decreased the mRNA level of ZEB2 (New Fig. 7A), so the baseline levels of ZEB2 in the shACSL4 group (New Fig. 7G) were very low and degradation is not obvious.

9) Figure 7D, the IP result of ACSL4 is not justified as there is no enrichment of ACSL4 in the IP compared to input. With the current data, it is hard to justify that there is any direct interaction. Moreover, based on IF data in Figure 3B-C, ACSL4 is exclusively localized in the cytoplasm, while ZEB2 is exclusively localized in the nucleus. It is hard to believe there is any direct interaction and mutual regulation.

We appreciate the reviewer’s thoughtful questions. We have repeated the IP assay and found that the enrichment of ACSL4 was observed in the IP process and added to new Fig. 7E as follows in Author response image 8. We also repeated the immunofluorescence assay in the MDA-MB-231 cells. We observed that ZEB2 can also be found in the cytoplasm and co-localized with ACSL in some certain regions of the cytoplasm as follows in Author response image 9 (Supplementary Fig. S11):

Author response image 8.

Author response image 9.

Reviewer #2 (Public Review):

In this study, the authors validated a positive feedback loop between ZEB2 and ACSL4 in breast cancer, which regulates lipid metabolism to promote metastasis.

Overall, the study is original, well structured, and easy to read. Despite the reliability of the data discussed in this article, there are still some deficiencies that need to be addressed through further explanation.

Major issues:

1) The authors demonstrated that ACSL4 regulates ZEB2 not only via a post-transcriptional mechanism but also via a transcriptional mechanism. The authors have not provided a comprehensive explanation of the specific mechanism in this paper. Therefore, it is recommended that the author delve into the potential mechanisms in the discussion section. For example, related mechanisms affecting ZEB2 ubiquitination degradation, as well as factors affecting ZEB2 upstream transcriptional regulation, etc.

We appreciate the positive comments and constructive suggestion from the reviewer. We have added the following paragraph in the second paragraph of the discussion section :

Interestingly, our RNA-seq data revealed that some ubiquitin E3 ligases, such as FBXO4, UBE3C, NEDD4, RBX1 etc. were significantly reduced in ACSL4 knockdown cells (Fig. S12). This result indicated that ACSL4 may reduce the ubiquitin of ZEB2 via down-regulating ubiquitin E3 ligase. Additionally, we found that ACSL4 promoted ZEB transcription as the mRNA level of ZEB2 was significantly reduced after ACSL4 knockdown. A recent study reported that LD-derived lipolysis provide acetyl-CoA for the epigenetic regulation of gene transcription. We observed that ACSL4 can also promote FAO, which generates acetyl-CoA for the epigenetic regulation. It is likely that ACSL4 regulates the ZEB2 mRNA level via lipid-epigenetic reprogramming mechanism, which is worth studying in the future.

2) To further clarify the interaction of ZEB2 and ACSL4, it is best to perform in vitro glutathione-S-transferase (GST) pulldown assay and immunofluorescence assay.

We appreciate the reviewer’s suggestion. We performed GST pull-down assay to examine whether ZEB2 and ACSL4 form a complex. GST pull-down assay confirmed the interaction of ZEB2 and ACSL4 as follows in Author response image 10 (Supplementary Fig. S10). We also performed immunofluorescence assay and found that ZEB2 was co-localized with ACSL in some certain regions of the cytoplasm as follows in Author response image 11. (Supplementary Fig. S11):

Author response image 10.

Author response image 11.

3) In Figure 7B, the protein level of ZEB2 seems not to be altered in BT549 BCSC cell line after the depletion of ACSL4.

We appreciate the reviewer to point out this problem. The protein level of ZEB2 in BT549 BCSC cell is not abundant as MDA-MB-231. We repeated the experiment and found that ZEB2 was reduced after the depletion of ACSL4 in BT549. We have replaced the Fig.7B as follows in Author response image 12:

Author response image 12.

4) EMT is characterized by changes in cell morphology, so the staining of cytoskeletons with Phalloidin is needed.

We appreciate the reviewer’s suggestion and performed the staining. The results show that the ACSL4 knockdown cells had a significantly smaller length to width ratio, which indicates the reversion of EMT process, than those of the control group (p<0.05). We have put the results in Supplementary Fig. S4 as follows in Author response image 13:

Author response image 13.

5) Additional breast cancer cases or cohorts (such as TMA) should be used to validate the positive correlation between ACSL4 and ZEB2 expression through IHC analysis.

We thank the reviewer for the suggestion. To better understand the positive correlation between ACSL4 and ZEB2 expression, we added more breast cancer cases up to 45 for IHC analysis and validated the positive correlation between ACSL4 and ZEB2. We have put the results into Fig 1 H and I as follows in Author response image 14:

Author response image 14.

Reviewer #3 (Public Review):

The manuscript by Lin et al. reveals a novel positive regulatory loop between ZEB2 and ACSL4, which promotes lipid droplets storage to meet the energy needs of breast cancer metastasis. It is of interest, however, some concerns should be addressed to strengthen the finding.

Major concerns:

1) The effect of ZEB2 overexpression is not fully demonstrated in the whole study. This point should be addressed.

We appreciate the positive comments and constructive suggestion from the reviewer. We have performed ZEB2 over-expressed MCF7 cell line. Over-expression of ZEB2 significantly enhanced the metastatic and invasive capacities of MCF7 cells. (Supplementary Fig. S5A and 5B).

Author response image 15.

1. Does the addition of oleate restore the ability of migration or invasion in ACSL4 knockdown cells?

We thank the reviewer for the question. To address this point, the oleate was added in the culture medium of ACSL4 knockdown cells. As expected, the addition of oleate obviously restores the invasive and metastatic capacities of ACSL4 knockdown cells by 33.12% and 18.61% respectively. We have added the results in the new Fig. 4D as follows in Author response image 16:

Author response image 16.

3) Which cellular compartment does ACSL4 localize in and interact with ZEB2 to stabilize ZEB2?

We thank the reviewer for the question. We have repeated the immunofluorescence assay in the MDA-MB-231 cells. We observed that ZEB2 can also be found in the cytoplasm and co-localized with ACSL in some certain regions of the cytoplasm (Supplementary Fig. S11):

4) The ubiquitination assay and Co-IP assay are just performed in HEK293T cells. This result should be confirmed in MDA-MB-231 cells or Taxol-resistant MCF-7 cells.

We appreciate the reviewer’s suggestion. We performed the ubiquitination assay and IP assay in MDA-MB-231 cells as follows. The results confirm that knockdown of ACSL4 obviously enhanced the ubiqutination of ZEB2. We have put the results into Fig. 7D and 7F as follows in Author response image 17:

Author response image 17.

5) How does ACSL4 regulate ZEB2 at the mRNA level？Please verify.

We thank the reviewer for the thoughtful question. A recent study reported that LD-derived lipolysis provide acetyl-CoA for the epigenetic regulation of gene transcription. We observed that ACSL4 can promote FAO, which generates acetyl-CoA for the epigenetic regulation. It is likely that ACSL4 regulates the ZEB2 mRNA level via lipid-epigenetic reprogramming mechanism, which is worth studying in the future and we had added the following sentences into the second paragraph in the discussion section :

Additionally, we found that ACSL4 promoted ZEB2 transcription as the mRNA level of ZEB2 was significantly reduced after ACSL4 knockdown. A recent study reported that LD-derived lipolysis provide acetyl-CoA for the epigenetic regulation of gene transcription. We observed that ACSL4 can also promote FAO, which can generate acetyl-CoA for the epigenetic regulation. It is likely that ACSL4 regulates the ZEB2 mRNA level via lipid-epigenetic reprogramming mechanism, which is worth studying in the future.

6) In Fig. 2F, the silencing efficiency for ACSL4 and ZEB2 should be shown. In addition, the protein level of ZEB2 or ACSL4 in shZEB2 and shZEB2+ACSL4 groups should also be addressed.

We appreciate the reviewer's suggestions. We have added the protein levels in Fig 2F and 2H as follows in Author response image 18:

Author response image 18.

7) What is the survival status of patients with both high expression of ACSL4 and ZEB2 in TCGA. In addition, more survival data from databases especially patients with both high expression of ACSL4 and ZEB2 are needed to analyze to support the finding.

We thank the reviewer for the constructive suggestion. We repeated the Kaplan-Meier survival analysis of TCGA RNA-seq data by using R4.3.0 software. The survival data show that the patients with both high expression of ACSL4 and ZEB2 have the worst prognosis in the four groups (P<0.05) ( New Fig. 1D-F).

Reviewer #1 (Recommendations For The Authors):

10) Only one siRNA/shRNA was used for knockdown in one cell line. Different siRNAs/shRNAs and multiple cell lines should be used to rule out off-target effects.

We appreciate the reviewer’s suggestion. We have test three siRNA and shRNA for the knockdown efficiency (negative control siRNA or ACSL4 and ZEB2 siRNA were from the company of GenePharma), we chose one sequence with the best knock-down effect.

Author response image 19.

11) Western blot data are required to justify the overexpression or knockdown efficiency of ACSL4 in cells in Figure 2 A-C.

We thank the reviewer for the suggestion. we have added the following western blot data in Figure 2:

Author response image 20.

12) In Figure 1G, there is a huge variation of the protein input, which makes the results not justified. The authors should repeat the experiments to ensure consistency and reproducibility of the results.

We appreciate the reviewer to point out this problem. Because this is the tissue samples of breast cancer patients. The results are affected by the tumor tissue composition between different patient sample, and it is difficult to obtain fresh tissues. In our paper, paraffin specimens have been used for IHC staining, and the results confirmed that ACSL4 and ZEB2 are positively correlated. We have put the results in the supplementary data.

Reviewer #2 (Recommendations For The Authors):

1) Data from Figure 1A showed the EMT transcription factor SNAIL was also among the top upregulated genes. Please explain why the association between ACSL4 and ZEB2 was studied instead of ACSL4 and SNAIL.

We appreciate the reviewer’s question. We had calculated the correlation between the ACSL4 and SNAIL by Pearson’s correlation test. The correlation of ACSL4 and SNAIL is 0.33, less than that of ZEB2. Bedsides, the binding motif analysis reveals that the consensus sequence of ZEB transcription family is within the ACSL4 promoter. Thus, we investigated the relationship between ACSL4 and ZEB2 in breast cancer cells.

Author response image 21

2) What is the limitation of your study? Please add some relevant description in the part of discussion.

We appreciate the reviewer’s suggestion. We have added the description of limitation of our study in the last paragraph of discussion section as follows:

The limitation of this study is the clinical samples is only 45. The future study should expand the clinical samples and cases to provide more clinical evidence for the crucial role of ACSL4 in breast cancer metastasis.

3). In Figure 3 Figure Legends part, the authors used the word "knockout", which is a description error.

We appreciate the reviewer’s advice. We have corrected "knockout" into "knockdown".

Reviewer #3 (Recommendations For The Authors):

Minor concerns:

1) In line 352-353, the statement about whether the high or low expression of ACSL4 and ZEB2 or the advanced breast cancer affects prognosis is inaccurate.

We appreciate the reviewer to point out this problem. We have corrected the statement into “We found that patients with higher ACSL4 or ZEB2 expression, especially those with simultaneous high expression had worse prognosis than those with lower expression ”.

2) The title of the seventh part of your results contains a logical error that is opposite to the experimental conclusion.

We truly appreciate the reviewer to point out this problem. We have changed the title of the seventh part of results to “ACSL4 regulates ZEB2 mRNA expression and protein stabilization”.

Author Response

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

Reviewer #1 (Public Review):

This study by Sokač et al. entitled "GENIUS: GEnome traNsformatIon and spatial representation of mUltiomicS data" presents an integrative multi-omics approach which maps several genomic data sources onto an image structure on which established deep-learning methods are trained with the purpose of classifying samples by their metastatic disease progression signatures. Using published samples from the Cancer Genome Atlas the authors characterize the classification performance of their method which only seems to yield results when mapped onto one out of four tested image-layouts.

Major recommendations:

• In its current form, GENIUS analysis is neither computationally reproducible nor are the presented scripts on GitHub generic enough for varied applications with other data. The GENIUS GitHub repository provides a collection of analysis scripts and not a finished software solution (e.g. command line tool or other user interface) (the presented scripts do not even suffice for a software prototype). In detail, the README on their GitHub repository is largely incomplete and reads analogous to an incomplete and poorly documented analysis script and is far from serving as a manual for a generic software solution (this claim was made in the manuscript).

We apologize for this oversight, and we have now invested considerable resources into making the documentation more detailed and accurate. We have created a new GitHub repository (https://github.com/mxs3203/GENIUS) that contains a small set of example data and all the necessary scripts to run GENIUS. The README file guides the user through each step of the GENIUS framework but it also contains a bash script that runs all the steps at once. When a user would like to use it on their own data, they need to replace the input data with their data but in the same format as the example input data. This is now fully documented in the README file. All scripts have arguments that can be used to point to custom data. The entire pipeline using example data can be run using run_genius.sh script. This script will produce CSV files and PNG files inside the ExtractWithIG folder containing attribution scores for every cancer type tested.

The authors should invest substantially into adding more details on how data can be retrieved (with example code) from the cited databases and how such data should then be curated alongside the input genome to generically create the "genomic image".

Data for analysis can be sourced from multiple locations, what we have used in our examples and for development was based on data from the TCGA. It can be retrieved from the official TCGA data hub or through Xena Browser (https://xenabrowser.net/). However, the data formats are generic, and similar data types (mutation, expression, methylation, copy number) can be obtained from multiple sources. We have added example data to demonstrate the layout, and we have a script included that creates the layout from standard mutation, expression, methylation and copy number data formats. We have substantially improved the annotations, including detailed descriptions of the data layout along with examples, and we have, as part of our validation, had an independent person test run the scripts using TCGA example data we provided on the new GitHub page.

In addition, when looking at the source code, parameter configurations for training and running various modules of GENIUS were hard-coded into the source code and users would have to manually change them in the source code rather than as command line flags in the software call. Furthermore, file paths to the local machine of the author are hard-coded in the source code, suggesting that images are sourced from a local folder and won't work when other users wish to replicate the analysis with other data. I would strongly recommend building a comprehensive command line tool where parameter and threshold configurations can be generically altered by the user via command line flags.

Apologies, we have changed the code and removed all hard-coded paths. All paths are now relative to the script using them. Furthermore, we made the config file more visible and easier to use. The example run can be found on the new github repository we linked in the previous comment.

We also inserted the following text in the manuscript

The GitHub repository contains example data and instructions on how to use the GENIUS framework.

A comprehensive manual would need to be provided to ensure that users can easily run GENIUS with other types of input data (since this is the claim of the manuscript). Overall, due to the lack of documentation and hard-coded local-machine folder paths it was impossible to computationally reproduce this study or run GENIUS in general.

Apologies, we have completely reworked the code base, and extensively annotated the code. We have also made highly detailed step-by-step instructions that should enable any user to run GENIUS on their own or public data.

• In the Introduction the authors write: "To correct for such multiple hypothesis testing, drastic adjustments of p-values are often applied which ultimately leads to the rejection of all but the most significant results, likely eliminating a large number of weaker but true associations.". While this is surely true for any method attempting to separate noise from signal, their argument fails to substantiate how their data transformation will solve this issue. Data transformation and projection onto an image for deep-learning processing will only shift the noise-to-signal evaluation process to the postprocessing steps and won't "magically" solve it during training.

The data transformation does not solve the problem of multiple hypothesis testing but it facilitates the use of computer vision algorithms and frameworks on rich multi-omics data. Importantly, transforming the data into genome images, training the model, and inspecting it with integrated gradients can be interpreted as running a single test on all of the data.

Analyzing multiomics data using classical statistical methods typically means that we perform extensive filtering of the data, removing genes with poor expression/methylation/mutation scores, and then e.g. perform logistic regression against a desired outcome, or alternatively, perform multiple statistical tests comparing each genomic feature independently against a desired outcome. Either way, information is lost during initial filtering and we must correct the analysis for each statistical test performed. While this increases confidence in whichever observation remains significant, it also undoubtedly means that we discard true positives. Additionally, classical statistical methods such as those mentioned here do not assume a spatial connection between data points, thus any relevant information relating to spatial organization is lost.

Instead, we propose the use of the GENIUS framework for multiomics analysis. The GENIUS framework is based on deep neural nets and relies on Convolutions and their ability to extract interactions between the data points. This particularly considers spatial information, which is not possible using classical statistical methods such as logistic regression where the most similar approach to this would include creating many models with many interactions.

Furthermore, integrated gradients is a non-parametric approach that simply evaluates the trained model relative to input data and output label, resulting in attribution for each input with respect to the output label. In other words, integrated gradients represent the integral of gradients with respect to inputs along the path from a given baseline to input. The integral is described in Author response image 1:

Author response image 1.

More about integrated gradients can be read on the Captum webpage (https://captum.ai/docs/introduction) or in original paper https://arxiv.org/abs/1703.01365.

Since we transformed the data into a data structure (genome image) that assumes a spatial connection between genes, trained the model using convolutional neural networks and analyzed the model using integrated gradients, we can treat the results without any parametric assumption. As a particular novelty, we can sort the list based on attribution score and take top N genes as our candidate biomarkers for the variable of interest and proceed with downstream analysis or potentially functional validation in an in vitro setting. In this manner, the reviewer is correct that the signal-to-noise evaluation is shifted to the post-processing steps. However, the benefit of the GENIUS framework is particularly that it enables integration of multiple data sources without any filtering, and with constructing a novel data structure that facilitates investigation of spatial dependency between data points, thus potentially revealing novel genes or biomarkers that were previously removed through filtering steps. However, further downstream validation of these hits remains critical.

We added the following paragraph to make this more clear

"Integrated Gradients is a non-parametric approach that evaluates the trained model relative to input data and output label, resulting in attribution scores for each input with respect to the output label. In other words, Integrated Gradients represent the integral of gradients with respect to inputs along the path from a given baseline. By using Integrated Gradients, we provide an alternative solution to the problem posed by performing multiple independent statistical tests. Here, instead of performing multiple tests, a single analysis is performed by transforming multiomics data into genome images, training a model, and inspecting it with Integrated Gradients. Integrated Gradients will output an attribution score for every gene included in the genome image and those can be ranked in order to retrieve a subset of the most associated genes relative to the output variable."

In addition, multiple-testing correction is usually done based on one particular data source (e.g. expression data), while their approach claims to integrate five very different genomic data sources with different levels and structures of technical noise. How are these applications comparable and how is the training procedure able to account for these different structures of technical noise? Please provide sufficient evidence for making this claim (especially in the postprocessing steps after classification).

The reviewer is correct that there will be different technical noise for each data source. However, each data source is already processed by standardized pipelines used for interpreting sequence-level data into gene expression, mutations, copy number alterations and methylation levels. Thus, sequence-level technical noise is not evaluated as part of the GENIUS analysis. Nevertheless, the reviewer is correct that sample-level technical noise, such as low tumor purity or poor quality sequencing, undoubtedly can affect the GENIUS predictions, as is true for all types of sequence analysis. As part of GENIUS, an initial data preprocessing step (which is performed automatically as part of the image generation), is that each data source is normalized within that source and linearly scaled in range zero to one (min-max scaling). This normalization step means that the impact of different events within and between data sources are comparable since the largest/smallest value from one data source will be comparable to the largest/smallest value from another data source.

Additionally, deep neural networks, particularly convolutional networks, have been shown to be very robust to different levels of technical noise (Jang, McCormack, and Tong 2021; Du et al. 2022). In the manuscript we show the attribution scores for different cancer types in figure 3B of the paper. Here, the top genes include established cancer genes such as P53, VHL, PTEN, APC and PIK3CA, indicating that the attribution scores based on GENIUS analysis is a valid tool to identify potential genes of interest. Furthermore, when focusing the analysis on predicting metastatic bladder cancer, we were able to show that of the top 10 genes with the highest attribution scores, 7 showed significant association with poor outcome in an independent validation cohort of mostly metastatic patients (shown in figure 4).

• I didn't find any computational benchmark of GENIUS. What are the computational run times, hardware requirements (e.g. memory usage) etc that a user will have to deal with when running an analogous experiment, but with different input data sources? What kind of hardware is required GPUs/CPUs/Cluster?

We apologize for not including this information in the manuscript. We added the following section in to the manuscript:

"Computational Requirements

In order to train the model, we used the following hardware configuration: Nvidia RTX3090 GPU, AMD Ryzen 9 5950X 16 core CPU, and 32Gb of RAM memory. In our study, we used a batch size of 256, which occupied around 60% of GPU memory. Training of the model was dependent on the output variable. For metastatic disease prediction, we trained the model for approximately 4 hours. This could be changed since we used early stopping in order to prevent overfitting. By reducing the batch size to smaller numbers, the technical requirements are reduced making it possible to run GENIUS on most modern laptops."

• A general comment about the Methods section: Models, training, and validation are very vaguely described and the source code on GitHub is very poorly documented so that parameter choices, model validation, test and validation frameworks and parameter choices are neither clear nor reproducible.

Apologies, we have updated the methods section with more details on models, training and validation. Additionally, we have moved the section on evaluating model performance from the methods section to the results section, with more details on how training was performed.

We also agree that the GitHub page is not sufficiently detailed and well structured. To remedy this, we have made a new GitHub page that only has the code needed for analysis, example input data, example runs, and environment file with all library versions. The GitHub repository is also updated in the manuscript.

The new GitHub page can be found on: https://github.com/mxs3203/GENIUS

Please provide a sufficient mathematical definition of the models, thresholds, training and testing frameworks.

We sincerely apologize, but we do not entirely follow the reviewers request on this regard. The mathematical definitions of deep neural networks are extensive and not commonly included in research publications utilizing deep learning. We have used PyTorch to implement the deep neural net, a commonly used platform, which is now referenced in the methods. The design of the deep learning network used for GENIUS is described in figure 1, and the relevant parameters are described in methods. The hyper parameters are described in the methods section, and are as follows:

"All models were trained with Adagrad optimizer with the following hyperparameters: starting learning rate = 9.9e-05 (including learning rate scheduler and early stopping), learning rate decay and weight decay = 1e-6, batch size = 256, except for memory-intensive chromosome images where the batch size of 240 was used."

• In chapter "Latent representation of genome" the authors write: "After successful model training, we extracted the latent representations of each genome and performed the Uniform Manifold Approximation and Projection (UMAP) of the data. The UMAP projected latent representations into two dimensions which could then be visualized. In order to avoid modeling noise, this step was used to address model accuracy and inspect if the model is distinguishing between variables of interest.". In the recent light of criticism when using the first two dimensions of UMAP projections with omics data, what is the evidence in support of the author's claim that model accuracy can be quantified with such a 2D UMAP projection? How is 'model accuracy' objectively quantified in this visual projection?

We apologize for not clarifying this. The UMAP was done on L, the latent vector, which by assumption should capture the most important information from the “genome image”. In order to confirm this, we plotted the first two dimensions of UMAP transformation and colored the points by the output variable. If the model was capturing noise, there should not be any patterns on the plot (randomized cancer-type panel). Since, in most cases, we do see an association between the first two UMAP dimensions and the output variable, we were confident that the model was not modeling (extracting) noise.

To clarify this, we changed the sentence in the manuscript so it is more clear that this is not an estimation of accuracy but only an initial inspection of the models:

The UMAP projected latent representations into two dimensions which could then be visualized. In order to avoid modeling noise, this step was used to inspect if the model is distinguishing between variables of interest.

• In the same paragraph "Latent representation of genome" the authors write: "We observed that all training scenarios successfully utilized genome images to make predictions with the exception of Age and randomized cancer type (negative control), where the model performed poorly (Figure 2B).". Did I understand correctly that all negative controls performed poorly? How can the authors make any claims if the controls fail? In general, I was missing sufficient controls for any of their claims, but openly stating that even the most rudimentary controls fail to deliver sufficient signals raises substantial issues with their approach. A clarification would substantially improve this chapter combined with further controls.

We apologize for not stating this more clearly. Randomized cancer type was used as a negative control since we expect that model would not be able to make sense of the data if predicting randomized cancer type. As expected, the model failed to predict the randomized cancer types. This can be seen in Figure 2C, where UMAP representations (based on the latent representation of the data, the vector L) are made for each output variable. Not seeing any patterns in UMAP shows that, as expected, the model does not know how to extract useful information from “genome image” when predicting randomized cancer type (as when randomly shuffling the labels there is no genomic information to decipher). Similar patterns were observed for Age, indicating that patient age cannot be determined from the multi-omics data. Conversely, when GENIUS was trained against wGII, TP53, metastatic status, and cancer type, we observed that samples clustered according to the output label.

Reviewer #2 (Public Review):

In this manuscript, Birkbak and colleagues use a novel approach to transform multi-omics datasets in images and apply Deep Learning methods for image analysis. Interestingly they find that the spatial representation of genes on chromosomes and the order of chromosomes based on 3D contacts leads to best performance. This supports that both 1D proximity and 3D proximity could be important for predicting different phenotypes. I appreciate that the code is made available as a github repository. The authors use their method to investigate different cancers and identify novel genes potentially involved in these cancers. Overall, I found this study important for the field.

The major points of this manuscript could be grouped in three parts:

1) While the authors have provided validation for their model, it is not always clear that best approaches have been used.

a) In the methods there is no mention of a validation dataset. I would like to see the authors training on a cancer from one cohort and predict on the same cancer from a different cohort. This will convince the reader that their model can generalise. They do something along those lines for the bladder cancer, but no performance is reported. At the very least they should withhold a percentage of the data for validation. Maybe train on 100 and validate on the remaining 300 samples. They might have already done something along these lines, but it was not clear from the methods.

Apologize for not being sufficiently clear in the manuscript. We did indeed validate the performance within the TCGA cohort, using holdout cross validation. Here, we trained the network on 75% of the cohort samples (N = 3825), and tested on the remaining 25% (N = 1276).

To make this more clear, we have rewritten section “GENIUS classification identifies tumors likely to become metastatic” as such:

"The omics data types included somatic mutations, gene expression, methylation, copy number gain and copy number loss. Using holdout type cross-validation, where we split the data into training (75%) and validation (25%), we observed a generally high performance of GENIUS, with a validation AUC of 0.83 for predicting metastatic disease (Figure 2B)."

We also added the following sentence in the legend of Figure 2:

"The x-axis represents epochs and y-axis represents AUC score of fixed 25% data we used for accuracy assessment within TCGA cohort."

The accuracy of GENIUS could not be validated on the other two bladder cohorts since they do not contain all the data for the creation of five-dimensional genome images. However, we were able to investigate if the genes with the highest attribution scores towards metastatic bladder cancer obtained based on the TCGA samples also showed a significant association with poor outcome in the two independent bladder cancer cohorts. Here, we observed that of the top 10 genes with the highest attribution scores, 5 were associated with poor outcome in the early stage bladder cancer cohort, and 7 were associated with poor outcome in the late stage/metastatic bladder cancer cohort.

b) It was not clear how they used "randomised cancer types as the negative control". Why not use normal tissue data or matched controls?

In the study, we built six models, one for each variable of interest. One of them was cancer type which performed quite well. In order to assess the model on randomized data, we randomized the labels of cancer type and tried predicting that. This served as “negative control” since we expected the model to perform poorly in this scenario. To make this more clear in the manuscript, we have expanded the description in the main text. We have also added the description of this to each supplementary plot to clarify this further.

While normal tissue and matched controls would have been an optimal solution, unfortunately, such data is not available.

c) If Figure 2B, the authors claim they have used cross validation. Maybe I missed it, but what sort of cross validation did they use?

We apologize for not being sufficiently clear. As described above, we used holdout cross-validation to train and evaluate the model. We clarified this in the text:

"Using holdout type cross-validation, where we split the data into training (80%) and validation (20%), we observed a generally high performance of GENIUS, with a mean validation AUC of 0.83 (Figure 2B)"

2) Potential improvement to the method

a) It is very encouraging the use of HiC data, but the authors used a very coarse approach to integrate it (by computing the chromosome order based on interaction score). We know that genes that are located far away on the same chromosome can interact more in 3D space than genes that are relatively close in 1D space. Did the authors consider this aspect? Why not group genes based on them being located in the same TAD?

We thank the reviewer for this suggestion and we will start looking into how to use TAD information to create another genome representation. In this study, we tried several genome transformations, which proved to be superior compared to a flat vector of features (no transformation). We are aware that squared genome transformation might not be optimal, so we designed the network that reconstructs the genome image during the training. This way, the genome image is optimized for the output variable of choice by the network itself. However, we note that the order of the genes themselves, while currently based on HiC, can be changed by the user. The order is determined by a simple input file which can be changed by the user with the argument “all_genes_included”. Thus, different orderings can be tested within the overall square layout. This is now detailed in the instructions on the new GitHub page.

The convolutional neural network uses a kernel size of 3x3, which captures the patterns of genes positioned close to each other but also genes that are far away from each other (potentially on another chromosome). Once convolutions extract patterns from the image, the captured features are used in a feed-forward neural network that makes a final prediction using all extracted features/patterns regardless of their location in the genome image.

We also inserted the following sentence in discussion:

"Given that spatial organization improved the prediction, we recognize that there may exist a more optimal representation of multi-omics data which should be explored further in future work. Potential methods for organizing gene orientation in a 2D image could consider integrating topologically associating domains[39] along with the spatial information from HiC. This is already possible to explore with the current implementation of GENIUS, where gene layout can be set manually by the user."

b) Authors claim that "given that methylation negatively correlates with gene expression, these were considered together". This is clearly not always the case. See for example https://genomebiology.biomedcentral.com/articles/10.1186/s13059-022-02728-5. What would happen if they were not considered together?

We thank the reviewer for this insightful comment. We agree with the reviewer that methylation does not always result in lower expression, although methylation levels in most cases should correlate negatively to RNA expression, but with a gene-specific factor. Indeed, there are tools developed that infer RNA expression based on methylation, making use of gene-specific correction factors. E.g. Mattesen et al (Mattesen, Andersen, and Bramsen 2021).

However, upon reflection we agree with the reviewer that we cannot assume for all genes that methylation equals low expression. Therefore, we have performed an analysis where we compared the methylation level to gene expression levels for all tested genes within bladder cancer. We computed Pearson’s correlation of 16,456 genes that have both methylation and expression scores. Of these, 8528 showed a negative correlation. After p-value correction, this resulted in 4774 genes where methylation was significantly negatively associated with expression. For these genes we performed the subsequent analysis in bladder cancer, where methylation and expression were considered together. This updated analysis has been included in supplementary figure 10, and the results section has been amended to reflect this. Overall, this analysis resulted in 4 of 10 genes being replaced in the downstream analysis. However, we note that the final results did not materially change, nor did the conclusions.

Author response image 2.

Correlation between gene-level methylation and gene expression in TCGA BLCA cohort

3) Interesting results that were not explained.

a) In Figure 3A methylation seems to be the most important omics data, but in 3B, mutations and expression are dominating. The authors need to explain why this is the case.

We apologize for not explaining this in more detail. Figure 3B shows the attribution scores scaled within the cancer type, where Figure 3A shows raw attribution scores for each data source included. The reason for this is that methylation and expression have in general, smaller attribution scores but more events where a single mutation often is characterized with large attribution scores and the rest of them with very small attribution. In order to make those numbers comparable and take into account biological differences between the cancer type, we scaled the scores within each cancer type.

To make this more clear we modified the first sentence in “Interpreting the GENIUS model classifying metastatic cancer biology” section:

"Analysing raw attribution scores we concluded the most informative data type overall regarding the development of metastatic disease was methylation (Figure 3A). …We also noticed that mutation data often had a single mutation with large attribution score where expression and methylation showed multiple genes with high attribution scores… … The normalization step is crucial to make results comparable as underlying biology is different in each cancer type included in the study."  

Reviewer #1 (Recommendations For The Authors):

• While I appreciate the creative acronym of the presented software solution (GENIUS), it may easily be confused with the prominent software Geneious | Bioinformatics Software for Sequence Data Analysis which is often employed in molecular life science research. I would suggest renaming the tool.

We appreciate the comment but prefer to keep the name. Given that the abbreviation is not exactly the same and the utility is different, we are confident that there will be no accidental mixup between these tools.

• A huge red flag is the evaluation of the input image design which clearly shows that classification power after training is insufficient for three out of four image layouts (and even for the fourth AUC is between 0.70-0.84 depending on the pipeline step and application). Could the authors please clarify why this isn't cherry-picking (we use the one layout that gave some form of results)? In light of the poor transformation capacity of this multi-omics data onto images, why weren't other image layouts tried and their classification performance assessed? Why should a user assume that this image layout that worked for this particular input dataset will also work with other datasets if image transformation is performing poorly in most cases?

We apologize for not describing this further in the manuscript. We wrote in the manuscript that we could not know what genome representation is optimal as it is difficult to know. A flat vector represents a simple (or no) transformation since we simply take all of the genes from all of the data sources and append them into a single list. Chromosome image and square image are two transformations we tried, and we focused on the square image since in our hands it showed superior performance relative to other transformations.

Reviewer #2 (Recommendations For The Authors):

Minor points:

1) Legends of supplementary Figures are missing.

We thank the reviewer for this comment and apologize for missing it. All legends have been added now.

2) For some tests the authors use F1 score while for other AUC, they should be consistent. Report all metrics for all comparisons or report one and justify why that only metric.

We apologize for not being sufficiently clear. AUC is a standard score used for binary classification, while the F1 score is used for multiclass classification. We have now described this in the methods section, and hope this is now sufficiently clear.

"When predicting continuous values, the model used the output from the activation function with the mean squared error loss function. When predicting multi-class labels, the performance measure was defined by the F1 score, a standard measure for multiclass classification that combines the sensitivity and specificity scores and is defined as the harmonic mean of its precision and recall. To evaluate model performance against the binary outcome, ROC analysis was performed, and the area under the curve (AUC) was used as the performance metric."

3) not sure how representation using UMAP in Figure 2C is helping understand the performance.

Apologies for the poor wording in the results section. The purpose of the UMAP representation was to visually inspect if the model was distinguishing between variables of interest, not to estimate model performance. We have rephrased the text in the methods section to make this clear:

"After successful model training, we extracted the latent representations of each genome and performed the Uniform Manifold Approximation and Projection (UMAP) of the data for the purpose of visual inspection of a model."

And

"In order to avoid modeling noise, this step was used to inspect if the model is distinguishing between variables of interest."

And also in the results section:

"In order to visually inspect patterns captured by the model, we extracted the latent representations of each genome and performed the Uniform Manifold Approximation and Projection (UMAP) of the data to project it into two dimensions."

4) Instead of pie chart in 3A, the authors should plot stacked barplots (to 100%) so it would be easier to compare between the different cancer types.

We thank the reviewer for the suggestion; however, since we wanted to compare the relative impact of each data source with each other, we used pie charts. Piecharts are often better for describing relative values, whereas bar plots are better for absolute values.

References

Du, Ruishan, Wenhao Liu, Xiaofei Fu, Lingdong Meng, and Zhigang Liu. 2022. “Random Noise Attenuation via Convolutional Neural Network in Seismic Datasets.” Alexandria Engineering Journal 61 (12): 9901–9.

Jang, Hojin, Devin McCormack, and Frank Tong. 2021. “Noise-Trained Deep Neural Networks Effectively Predict Human Vision and Its Neural Responses to Challenging Images.” PLoS Biology 19 (12): e3001418.

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Author response:

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

Review #1:

(1) It would be helpful to explain the criteria for choosing a given number of clusters and for accepting the final clustering solution more clearly. The quantitative results (silhouette plots, Rand index) in Supplementary Figure 2 should perhaps be included in the main figure to justify the parameter choices and acceptance of specific clustering solutions.

We revised the text and added labels to the original Supplementary Figure 2 (now main Figure 4) to clarify how we arrived at the best settings for random-seed clustering. 

(2) It would be helpful to show how the activity profiles in Figure 3 would look like for 3 or 5 (or 6) clusters, to give the reader an impression of how activity profiles recovered using different numbers of clusters would differ.

We added a new figure (Supplementary Figure 4) that shows 5- and 6-cluster results. Note that the same three subpopulations in Figure 3 were reliably identified as distinct clusters even with alternative settings, corroborating the results in the tSNE space (Supplementary Figure 3). 

(3) The authors attempt to link the microstimulation effects to the presence of functional neuron clusters at the stimulation site. How can you rule out that there were other, session-specific factors (e.g., related to the animal's motivation) that affected both neuronal activity and behavior? For example, could you incorporate aspects of the monkey's baseline performance (mean reaction time, fixation breaks, error trials) into the analysis?

We tested the potential influences of monkeys’ motivational states on our observations using two sets of analysis. First, we examined whether motivational state modulated the likelihood of observing a specific type of neural activity in STN. We focused on three measurements of motivational states: the rate of fixation break, the overall error rate, and mean RT. We found that none of these measurements differed significantly among sessions when we encountered different subpopulations (new Supplemental Figure 7), suggesting that motivational state alone cannot explain the differences in activity patterns of the four subpopulations. 

Second, we examined how motivational state may be reflected in the microstimulation results. To clarify, because we interleaved trials with and without microstimulation, the microstimulation effects cannot be solely explained by session-specific factors. However, it is possible that motivational state can modulate the magnitude of microstimulation effects. We performed correlation analysis between microstimulation effects (difference in each fitted DDM parameter between trials with and without microstimulation) and motivational state (fixation break, error rate, mean RT on trials without microstimulation). We did not find significant correlation for any combination (Supplemental Table 1). These results suggest that the motivational state of the monkey had little influence on our recording and microstimulation results. However, because our monkeys operated within a narrow range of strong engagement on the task, we cannot rule out the possibility that STN activity or microstimulation effects could change significantly if the monkeys were not as engaged. We have added these results in a new section titled “Heterogeneous activity patterns and microstimulation effects cannot be explained by variations in motivational state”. 

(4) Line 84: What was the rationale for not including both coherence and reaction time in one multiple regression model?

On the task we used, RT depends strongly on coherence in a nonlinear fashion (e.g., example behavior in now Figure 5). We thus performed regressions using coherence and RT separately. We revised the text in Methods to clarify our rationale (lines 470-473):

“To quantitatively measure each neuron’s task-related modulation, we performed two multiple linear regressions for each running window, separately for coherence and RT because monkeys’ RT strongly depends on coherence on our task:”

Review #2:

The interpretation of the results, and specifically, the degree to which the identified clusters support each model, is largely dependent on whether the artificial vectors used as model-based clustering seeds adequately capture the expected behavior under each theoretical model. The manuscript would benefit from providing further justification for the specific model predictions summarized in Figure 1B.

We added information on the original figure/equations that were the basis of the artificial vectors we constructed for clustering analysis and their abbreviated summary in Figure 1B (first paragraph in section “STN subpopulations can support previously theorized functions”). These vectors were meant to capture prominent features of the predicted activity patterns, in the forms of choice, time, and motion strength dependencies. We also emphasize that we obtained very similar results using random clustering seeds.

Further, although each cluster's activity can be described in the context of the discussed models, these same neural dynamics could also reflect other processes not specific to the models. That is, while a model attributing the STN's role to assessing evidence accumulation may predict a ramping up of neural activity, activity ramping is not a selective correlate of evidence accumulation and could be indicative of a number of processes, e.g., uncertainty, the passage of time, etc. This lack of specificity makes it challenging to infer the functional relevance of cluster activity and should be acknowledged in the discussion.

We thank the reviewer for pointing out the alternative interpretation of these modulation patterns. We have added this caveat in the Discussion (lines 398-401): “It is also possible that the ramping activity reflects alternative roles for the STN in the evaluation of the decision process, the tracking of elapsed time, or both. How these possible roles relate to those of caudate neurons awaits further investigation (Fan et al., 2024)”. 

Additionally, although the effects of STN microstimulation on behavior provide important causal evidence linking the STN to decision processes, the stimulation results are highly variable and difficult to interpret. The authors provide a reasonable explanation for the variability, showing that neurons from unique clusters are anatomically intermingled such that stimulation likely affects neurons across several clusters. It is worth noting, however, that a substantial body of literature suggests that neural populations in the STN are topographically organized in a manner that is crucial for its role in action selection, providing "channels" that guide action execution. The authors should comment on how the current results, indicative of little anatomical clustering amongst the functional clusters, relate to other reports showing topographical organization.

We thank the reviewer for raising this important point. We have added the following text in the Discussion:

“The intermingled subpopulations may appear at odds with the conventional idea of topography in how the STN is organized. For example, the “tripartite model” suggests that STN is segregated by motor, associative, and limbic functions (Parent and Hazrati, 1995); afferents from motor cortices and neurons related to different types of movements are largely somatotopically organized in the STN (DeLong et al., 1985; Nambu et al., 1996); and certain molecular markers are expressed in an orderly pattern in the STN (reviewed in Prasad and Wallén-Mackenzie, 2024). Because we focused on STN neurons that were responsive on a single oculomotor decision task, our sampling was likely biased toward STN subdivisions related to associative function and oculomotor movements. As such, our results do not preclude the presence of topography at a larger scale. Rather, our results underscore the importance of activity patternbased analysis, in addition to anatomy-based analysis, for understanding the functional organization of the STN.”

Figure 3 is referenced when describing which cluster activity is choice/coherence dependent, yet it is unclear what specific criteria and measures are being used to determine whether activity is choice/coherence "dependent." Visually, coherence activity seems to largely overlap in panel B (top row). Is there a statistically significant distinction between low and high coherence in this plot? The interpretation of these plots and the methods used to determine choice/coherence "dependence" needs further explanation.

We added a new figure (Sup Figure 3) that shows the summary of choice and coherence modulation, based on multiple linear regression analysis, for each subpopulation separately. We also updated the description of these activity patterns in Results (lines 122-130):

In general, the association between cluster activity and each model could be more directly tested. At least two of the models assume coordination with other brain regions. Does the current dataset include recordings from any of these regions (e.g., mPFC or GPe) that could be used to bolster claims about the functional relevance of specific subpopulations? For example, one would expect coordinated activity between neural activity in mPFC and Cluster 2 according to the Ratcliff and Frank model.

We agree completely that simultaneous recordings of STN and its afferent/efferent regions (such as mPFC, GPe, SNr, and GPi) would provide valuable insights into the specific roles of STN and the basal ganglia as a whole. Such recordings are outside the scope of the current study but are in our future plans. 

Additionally, the reported drift-diffusion model (DDM) results are difficult to interpret as microstimulation appears to have broad and varied effects across almost all the DDM model parameters. The DDM framework could, however, be used to more specifically test the relationships between each neural cluster and specific decision functions described in each model. Several studies have successfully shown that neural activity tracks specific latent decision parameters estimated by the DDM by including neural activity as a predictor in the model. Using this approach, the current study could examine whether each cluster's activity is predictive of specific decision parameters (e.g., evidence accumulation, decision thresholds, etc.). For example, according to the Ratcliff and Frank model, activity in cluster 2 might track decision thresholds.

We thank the reviewer for the suggested analysis. Because including the neural activity in the model substantially increases model fitting time, we performed a preliminary round of model fitting for 15 neurons (5 neurons closest to each of the cluster centroids). For each neuron, we measured the average firing rates in three windows: 1) a 350 ms window starting from dots onset (“Dots”), 2) a 350 ms window ending at saccade onset (“Presac”), and 3) a variable window starting from dots onset and ending at 100 ms before saccade onset (“Fullview”). For each window, the firing rates were z-scored across trials.  We incorporated the firing rates into two model types. In the “DV” type, the firing rates were assumed to influence three DDM parameters related to evidence accumulation: k, me, and z. In the “Bound” type, the firing rates were assumed to influence three DDM parameters related to decision bound: a, B_alpha, and B_d. In total, we fitted six combinations of firing rates and model types to each neuron. For comparison, we also fitted the standard model without incorporating firing rates. 

As shown in Author response image 1, firing rates of single STN neurons had minimal contributions to the fits. With the exception of one neuron, AIC values were greater for model variants including firing rates than the standard model (Author response image 1A), indicating that including firing rate did not improve the fits. For all neurons, the actual fitted coefficients for firing rates were several degrees of magnitude smaller than the corresponding DDM parameter (Author response image 1B; note the range of y axis), indicating that the trial-by-trial variation in firing rate had little influence on the evidence accumulation- or decision bound-related parameters. Based on these preliminary fitting results, we believe that a single STN neuron does not have strong enough influence on the overall evidence accumulation or decision bound to be detected with the model fitting method.  We therefore did not expand the fitting analysis to all neurons. 

Author response image 1.

Firing rates of a single STN neuron did not substantially influence decision-related DDM parameters. A, Differences in AIC between DDM variants that included firing rate-dependent terms and the standard DDM. Red dahsed line: difference = -3. Each column represents results from one unit. B, Fitted coefficients for firing rate-related terms were near zero. Note the range of y axis. Values for the top and bottomw panels were obtained from "DV"- and "Bound"-type models, respectively. See text for more details.

We emphasize, however, that the apparent negative results do not necessarily argue against a causal role of the STN in decision making, rather, these results more likely reflect the methodological limitation: because we used a single task context, the monkeys’ natural trial-by- trial variations in the DDM components may be too small. A better design would be to manipulate task contexts to induce larger changes in evidence accumulation or decision bounds and then test for a correlation between single-neuron firing rates and these changes. We are currently using such a design in a follow-up study. 

The table in Figure 1B nicely outlines the specific neural predictions for each theoretical model but it would help guide the reader if the heading for each column also included a few summary words to remind the reader of the crux of each theory, e.g. "Ratcliff+Frank 2012 (adjusted decision-bounds)"

We thank the reviewer for this suggestion. We considered implementing this but eventually decided not to add more headings to the column, because the predicted STN functions of the three models cannot all be succinctly summarized. We thus prefer to include more detailed descriptions in the main text, instead of in the figure. 

The authors frequently refer to contralateral vs. ipsilateral decisions but never explicitly state what this refers to, i.e. contralateral relative to what (visual field, target direction, recording site, etc.)? The reader can eventually deduce that this means contralateral to the recording site but this should be explicitly stated for clarity.

We added in Methods: 

Line 483: “Contralateral/ipsilateral choices refer to saccades toward the targets contralateral/ipsilateral to the recording sites, respectively.” 

Line 535: Contralateral/ipsilateral choices refer to saccades toward the targets contralateral/ipsilateral to the microstimulation sites, respectively.”

Again, for clarity, it would be helpful to explicitly define what the authors mean by "sensitive to choice" when referring to Figure 1B as this could be interpreted to mean left/right or ipsilateral/contralateral.

In the context of Figure 1B, “sensitive to choice” means showing different responses for the two choices in our 2AFC task, regardless of the task geometry. We added explanation in the figure caption.

Color bar labels would be helpful to include in all figures that include plots with color bars.

We apologize for omitting the labels. They are added to Figure 2B and C, Supplemental Fig. 1.  

The authors should briefly note what a "lapse term" is when describing the logistic function results.

We revised the text in Results (lines 184-186) and Methods (line 527) to clarify that lapse terms were used to capture errors independent of motion strength.

Are the 3 example sessions in Figure 4 stimulating the same STN site and/or the same monkey? This information should be noted in the caption or main text.

We revised the caption: “A-C, Monkey’s choice (top) and RT (bottom) performance for trials with (red) and without (black) microstimulation for three example sessions (A,B: two sites in monkey C; C: monkey F).”

Figure 3B the authors note that "the last cluster shows little task-related modulation" - what criteria are they using to make this conclusion? By eye, the last cluster and cluster 1 seem to show a similar degree of modulation when locked to motion onset.

We added a new figure (Suppl Figure 2) that shows the summary of choice and coherence modulation, based on multiple linear regression analysis, for each subpopulation separately. 

Reviewer #3:

We have grouped the reviewer’s public and specific comments by content. 

First, the interpretation of the neural subpopulations' activity patterns in relation to the computational models should be clarified, as the observed patterns may not directly correspond to the specific signals predicted by the models. The authors claim that the first subpopulation of STN neurons reflects the normalization signal predicted by the model of Bogacz and Gurney (2007). However, the observed activity patterns only show choice- and coherence-dependent activity, which may represent the input to the normalization computation rather than its output. The authors should clarify this point and discuss the limitations of their interpretation. 

We agree with the reviewer that the choice- and coherence-dependent activity pattern does not sufficiently indicate a normalization computation. We interpreted such activity as satisfying a necessary condition for, and therefore consistent with, the theoretical model proposed by Bogacz and Gurney. We have reviewed the text to ensure that we never made the claim that the first subpopulation mediates the normalization.   

Second, the authors could consider using a supervised learning method to more explicitly model the pattern correlations between the three profiles. The authors used k-means clustering to identify STN subpopulations. Given the clear distinction between the three types of neural firing patterns, a supervised learning method (e.g., a generalized linear model) could be used as a more explicit encoding model to account for the pattern correlations between the three profiles.

We used two approaches to examine the different response profiles. The “random-seed” approach used non-supervised clustering to probe the functional organization of STN neurons, with no a priori assumption about how many subpopulations may be present. The “model-seed” approach is similar in spirit to what the reviewer suggested: we defined artificial vectors, akin to regressors in a generalized linear model, that showed key modulation features as predicted by previous theoretical models. We then projected the neurons’ activity profiles onto these vectors, akin to performing a regression analysis.   

Third, a neural population model could be employed to better understand how the STN population jointly contributes to decision-making dynamics. The single-neuron encoding analysis reveals mixed effects from multiple decision-related functions. To better understand how the STN population jointly contributes to the decision-making process, the authors could consider using a neural population model (e.g., Wang et al., 2023) to quantify the population dynamics.

We agree with the reviewer that a neural population model would be helpful for testing our understanding of the roles of STN. However, we believe that this is premature at the moment because we have no knowledge about how these different subpopulations interact with each other within STN, nor how they interact with other basal ganglia nuclei. We hope our results provide a foundation for future experiments that can provide more specific insights in the roles of each subpopulation, which can then be tested in a neural population model as the reviewer suggested.  

Finally, the added value of the microstimulation experiments should be more directly addressed in the Results section, as the changes in firing patterns compared to the original patterns are not clearly evident. The microstimulation results (Figure 7A) do not show significant changes in firing patterns compared to the original patterns (Figure 3B). As microstimulation is used to identify the hypothetical role of the STN beyond the correlational analysis, the authors should more directly address the added value of these experiments in the Results section.

We apologize for the confusion. The average firing rates at the top of original Figure 7A (now Figure 8A) were obtained in recordings just before microstimulation, to document which neuron subpopulation was near the stimulation electrode. We were not able to obtain recordings from the same neurons during microstimulation.  

The ordering of the three hypotheses in the Introduction (1) adjusting decision bounds, (2) computing a normalization signal, (3) implementing a nonlinear computation to improve decision bound adjustment, is inconsistent with the order in which they are addressed in the Results section (2, 1, 3). To improve clarity and readability, the authors should consider presenting the hypotheses and their corresponding results in a consistent order throughout the manuscript.

We thank the reviewer for this suggestion. We have reordered the text in Introduction to be consistent.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors set out to explore the role of upstream open reading frames (uORFs) in stabilizing protein levels during Drosophila development and evolution. By utilizing a modified ICIER model for ribosome translation simulations and conducting experimental validations in Drosophila species, the study investigates how uORFs buffer translational variability of downstream coding sequences. The findings reveal that uORFs significantly reduce translational variability, which contributes to gene expression stability across different biological contexts and evolutionary timeframes.

We thank the reviewer for carefully reading our manuscript and providing thoughtful and constructive feedback. We believe the manuscript has been significantly improved by incorporating your suggestions. Please find our detailed responses and corresponding revisions below.

Strengths:

(1) The study introduces a sophisticated adaptation of the ICIER model, enabling detailed simulation of ribosomal traffic and its implications for translation efficiency.

(2) The integration of computational predictions with empirical data through knockout experiments and translatome analysis in Drosophila provides a compelling validation of the model's predictions.

(3) By demonstrating the evolutionary conservation of uORFs' buffering effects, the study provides insights that are likely applicable to a wide range of eukaryotes.

We appreciate your positive feedback and thoughtful summary of the strengths of our study.

Weaknesses:

(1) Although the study is technically sound, it does not clearly articulate the mechanisms through which uORFs buffer translational variability. A clearer hypothesis detailing the potential molecular interactions or regulatory pathways by which uORFs influence translational stability would enhance the comprehension and impact of the findings.

Thanks for your constructive comments. In the Discussion section of our previous submission (Original Lines 470-489), we proposed that uORFs function as “molecular dams” to smooth out fluctuations in ribosomal flow toward downstream CDS regions, primarily via mechanisms involving ribosome collision and dissociation. To further address your concern, we have expanded the Discussion and included a new model figure (Fig. 9) to more clearly articulate the potential biological and mechanistic basis by which translating 80S ribosomes may induce the dissociation of 40S ribosomes. The revised section (Lines 540–557) now reads:

“Ribosome slowdown or stalling on mRNA due to rare codons [56,96-98] or nascent blocking peptides [99-102] frequently triggers ribosome collisions genome-wide [103-105]. Such collisions, especially among elongating 80S ribosomes, often activate ribosome quality control (RQC) pathways that recognize collision interfaces on the 40S subunit, leading to ribosomal subunit dissociation and degradation [106-108]. In mammals, ZNF598 specifically identifies collided ribosomes to initiate ubiquitin-dependent protein and mRNA quality control pathways [109-113]. Analogously, yeast employs Hel2-mediated ubiquitination of uS10, initiating dissociation via the RQC-trigger complex (RQT) [114]. Furthermore, the human RQT (hRQT) complex recognizes ubiquitinated ribosomes and induces subunit dissociation similarly to yeast RQT [115]. However, transient ribosome collisions can evade RQC by promoting resumed elongation through mechanical force provided by trailing ribosomes, thereby mitigating stalling [116]. Beyond 80S collisions, evidence increasingly highlights a distinct collision type involving scanning 40S subunits or pre-initiation (43S) complexes. Recently, an initiation RQC pathway (iRQC) targeting the small ribosomal subunit (40S) has been described, particularly involving collisions between scanning 43S complexes or between stalled 43S and elongating 80S ribosomes (Figure 9B) [117,118]. During iRQC, E3 ubiquitin ligase RNF10 ubiquitinates uS3 and uS5 proteins, resulting in 40S degradation [118]. This mechanism aligns closely with our ICIER model, proposing collision-driven 43S dissociation in the 5' UTRs. Future studies exploring these mechanisms in greater detail will clarify how uORFs modulate translational regulation through buffering effects.”

(2) The study could be further improved by a discussion regarding the evolutionary selection of uORFs. Specifically, it would be beneficial to explore whether uORFs are favored evolutionarily primarily for their role in reducing translation efficiency or for their capability to stabilize translation variability. Such a discussion would provide deeper insights into the evolutionary dynamics and functional significance of uORFs in genetic regulation.

Thank you for this insightful suggestion. We agree that understanding whether uORFs are evolutionarily favored for their role in translational repression or for their capacity to buffer translational variability is a compelling and unresolved question. Our study suggests that translational buffering, rather than translational repression alone, can also drive evolutionary selection favoring uORFs, although it remains challenging to empirically disentangle these functions due to their inherent linkage. We have expanded the discussion in the revised manuscript to address this point in more detail (Lines 494-513), which is reproduced as follows:

“Previous studies have shown that a significant fraction of fixed uORFs in the populations of D. melanogaster and humans were driven by positive Darwinian selection 63,67, suggesting active maintenance through adaptive evolution rather than purely neutral or deleterious processes. While uORFs have traditionally been recognized for their capacity to attenuate translation of downstream CDSs, accumulating evidence now underscores their critical role in stabilizing gene expression under fluctuating cellular and environmental conditions [43,55,56]. Whether the favored evolutionary selection of uORFs acts primarily through their role in translational repression or translational buffering remains a compelling yet unresolved question, as these two functions are inherently linked. Indeed, highly conserved uORFs tend to be translated at higher levels, resulting not only in stronger inhibition of CDS translation [34,45,67] but also in a more pronounced buffering effect, as demonstrated in this study. This buffering capacity of uORFs potentially provides selective advantages by reducing fluctuations in protein synthesis, thus minimizing gene-expression noise and enhancing cellular homeostasis. This suggests that selection may favor uORFs that contribute to translational robustness, a hypothesis supported by findings in yeast and mammals showing that uORFs are significantly enriched in stressresponse genes and control the translation of certain master regulators of stress responses [41,42,94,95]. Our study suggests that translational buffering, rather than translational repression alone, can also drive evolutionary selection favoring uORFs, although it remains challenging to empirically disentangle these functions. Future comparative genomic analyses, coupled with experimental approaches such as ribosome profiling and functional mutagenesis, will be crucial in elucidating the precise evolutionary forces driving uORF conservation and adaptation.”

Reviewer #2 (Public review):

uORFs, short open reading frames located in the 5' UTR, are pervasive in genomes. However, their roles in maintaining protein abundance are not clear. In this study, the authors propose that uORFs act as "molecular dam", limiting the fluctuation of the translation of downstream coding sequences. First, they performed in silico simulations using an improved ICIER model, and demonstrated that uORF translation reduces CDS translational variability, with buffering capacity increasing in proportion to uORF efficiency, length, and number. Next, they analzed the translatome between two related Drosophila species, revealing that genes with uORFs exhibit smaller fluctuations in translation between the two species and across different developmental stages within the same specify. Moreover, they identified that bicoid, a critical gene for Drosophila development, contains a uORF with substantial changes in translation efficiency. Deleting this uORF in Drosophila melanogaster significantly affected its gene expression, hatching rates, and survival under stress condition. Lastly, by leveraging public Ribo-seq data, the authors showed that the buffering effect of uORFs is also evident between primates and within human populations. Collectively, the study advances our understanding of how uORFs regulate the translation of downstream coding sequences at the genome-wide scale, as well as during development and evolution.

The conclusions of this paper are mostly well supported by data, but some definitions and data analysis need to be clarified and extended.

We thank the reviewer for the thoughtful and constructive review. Your summary accurately captures the key findings of our study. We have carefully addressed all your concerns in the revised manuscript, and we believe it has been significantly improved based on your valuable input.

(1) There are two definitions of translation efficiency (TE) in the manuscript: one refers to the number of 80S ribosomes that complete translation at the stop codon of a CDS within a given time interval, while the other is calculated based on Ribo-seq and mRNA-seq data (as described on Page 7, line 209). To avoid potential misunderstandings, please use distinct terms to differentiate these two definitions.

Thank you for highlighting this important point, and we apologize for the confusion. The two definitions of translation efficiency (TE) in our manuscript arise from methodological differences between simulation and experimental analyses. To clarify, in the revised manuscript, we use “translation rate” in the context of simulations to describe the number of 80S ribosomes completing translation at the CDS stop codon per unit time. We retain the conventional “translation efficiency (TE)” for Ribo-seq–based measurements. 

In this revised manuscript, we have added a more detailed explanation of TE in the revised manuscript (Lines 202–206), which now reads:

“For each sample, we followed established procedures [62-66] to calculate the translational efficiency (TE) for each feature (CDS or uORF). TE serves as a proxy for the translation rate at which ribosomes translate mRNA into proteins, typically quantified by comparing the density of ribosome-protected mRNA fragment (RPF) to the mRNA abundance for that feature (see Materials and Methods).”

(2) Page 7, line 209: "The translational efficiencies (TEs) of the conserved uORFs were highly correlated between the two species across all developmental stages and tissues examined, with Spearman correlation coefficients ranging from 0.478 to 0.573 (Fig. 2A)." However, the authors did not analyze the correlation of translation efficiency of conserved CDSs between the two species, and compare this correlation to the correlation between the TEs of CDSs. These analyzes will further support the authors conclusion regarding the role of conserved uORFs in translation regulation.

In the revised manuscript, we have incorporated a comparison of translational efficiency (TE) correlations for conserved CDSs between the two species. We found that CDSs exhibit significantly higher interspecific TE correlations than uORFs, with Spearman’s rho ranging from 0.588 to 0.806. This suggests that uORFs tend to show greater variability in TE than CDSs, consistent with our model in which uORFs buffer fluctuations in downstream CDS translation. The updated results were included in the revised manuscript (Lines 223-227) as follows:

“In contrast, TE of CDSs exhibited a significantly higher correlation between the two species in the corresponding samples compared to that of uORFs, with Spearman’s rho ranging from 0.588 to 0.806 (P = 0.002, Wilcoxon signed-rank test; Figure 2A). This observation is consistent with our simulation results, which indicate that uORFs experience greater translational fluctuations than their downstream CDSs.”

(3) Page 8, line 217: "Among genes with multiple uORFs, one uORF generally emerged as dominant, displaying a higher TE than the others within the same gene (Fig. 2C)." The basis for determining dominance among uORFs is not explained and this lack of clarification undermines the interpretation of these findings.

Thank you for pointing this out. We apologize for the confusion. In our study, a “dominant” uORF is defined as the one with the highest translation efficiency (TE) among all uORFs within the same gene. This designation is based solely on TE, which we consider a key metric for uORF activity, as it directly reflects translational output and potential regulatory impact. We have revised the manuscript to clarify this definition (Lines 232–244), now stating:

“Among genes with multiple uORFs, we defined the uORF with the highest TE as the dominant uORF for that gene, as TE is one of the most relevant metrics for assessing uORF function 45,67…… These results suggest that genes with multiple uORFs tend to retain the same dominant uORF across developmental stages, indicating that the dominant uORFs may serve as the key translational regulator of the downstream CDS.”

(4) According to the simulation, the translation of uORFs should exhibit greater variability than that of CDSs. However, the authors observed significantly fewer uORFs with significant TE changes compared to CDSs. This discrepancy may be due to lower sequencing depth resulting in fewer reads mapped to uORFs. Therefore, the authors may compare this variability specifically among highly expressed genes.

Thank you for this thoughtful observation. We agree that the lower proportion of uORFs showing significant TE changes compared to CDSs, as reported in Table 1, appears inconsistent with our conclusion that uORFs exhibit greater translational variability. However, this discrepancy is largely attributable to differences in sequencing depth and feature length—uORFs are generally much shorter and more weakly expressed than CDSs, resulting in fewer mapped reads and reduced statistical power (Figure S18A).

To address this issue, we first followed your suggestion and restricted our analysis to genes with both mRNA and RPF RPKM values above the 50th percentile in D. melanogaster and D. simulans. While this filtering increased the total proportion of features with significant TE changes (due to improved read coverage), the proportion of significant uORFs still remained lower than that of CDSs (Table R1). This suggests that even among highly expressed genes, the disparity in read counts between uORFs and CDSs persists (Figure S18B), and thus the issue is not fully resolved.

To better capture biological relevance, we compared the absolute values of log2(TE changes) between D. melanogaster and D. simulans for uORFs and their corresponding CDSs. Across all samples, uORFs consistently exhibit larger TE shifts than their downstream CDSs, supporting our model that uORFs act as translational buffers (Figure 3B).

We have made relevant changes to report the new analysis in this revised manuscript. Specifically, in our original submission, we stated this observation with the sentence “The smaller number of uORFs showing significant TE changes compared to CDSs between D. melanogaster and D. simulans likely reflects their shorter length and reduced statistical power, rather than indicating that uORFs are less variable in translation than CDSs.” To make this point clearer, in the revised version (Lines 275-284), we rephrased this sentence which read as follows: 

“Note that due to their shorter length and generally lower TE, uORFs had considerably lower read counts than CDSs, limiting the statistical power to detect significant interspecific TE differences for uORFs. This trend consistently holds whether analyzing all expressed uORFs (Figure S18A) or only highly expressed genes (Figure S18B). Thus, the fewer uORFs showing significant TE divergence likely reflects lower read counts and statistical sensitivity rather than reduced translational variability relative to CDSs. In fact, the absolute values of log2(fold change) of TE for uORFs between D. melanogaster and D. simulans were significantly greater than those observed for corresponding CDSs across all samples (P < 0.001, Wilcoxon signed-rank test; Figure 3B), suggesting that the magnitude of

TE changes in CDSs is generally smaller than that in uORFs, due to the buffering effect of uORF.”

Author response table 1.

Proportion of uORFs and CDSs with significant TE changes before and after selecting HEGs

(5) If possible, the author may need to use antibodies against bicoid to test the effect of ATG deletion on bicoid expression, particularly under different developmental stages or growth conditions.

According to the authors' conclusions, the deletion mutant should exhibit greater variability in bicoid protein abundance. This experiment could provide strong support for the proposed mechanisms.

Thank you for this excellent suggestion. We fully agree that testing Bcd protein levels across developmental stages or stress conditions using antibodies would be a strong validation of our model, which predicts greater variability in Bcd protein abundance upon uORF deletion.

In fact, we attempted such experiments in both wild-type and mutant backgrounds. However, we encountered substantial difficulties in obtaining a reliable anti-Bcd antibody. Some Bcd antibodies referenced in the published literature were homemade and often shared among research groups as gifts [1-3] and some commercially available antibodies cited in previous studies are no longer supplied by vendors [4-6]. We managed to obtain a custom-made antibody from Professor Feng Liu, but unfortunately, it produced inconsistent and unsatisfactory results. Despite considerable effort—including during the COVID-19 pandemic—we were unable to identify a reagent suitable for robust and reproducible detection of Bcd protein.

As an alternative, we used sucrose gradient fractionation followed by qPCR to directly measure the translation efficiency of bicoid in vivo. We believe this approach offers a clear and quantitative readout of translational activity, and it avoids potential confounding from protein degradation, which may vary across conditions and developmental stages. Nonetheless, we recognize the value of antibody-based validation and will pursue this direction in future work if reliable antibodies become available. We have added this limitation to the revised Discussion section (Lines 563–568) as follows:

“We demonstrated that the bcd uORF represses CDS translation using sucrose gradient fractionation followed by qPCR—an approach that directly measures translation efficiency while minimizing confounding from RNA/protein degradation. However, detecting Bcd protein levels with antibodies across developmental stages or conditions in the mutants and wild-type controls would provide an even stronger validation of our model and should be explored in future studies.”

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

(1) The authors should provide a more detailed explanation for the modifications made to the ICIER model. Specifically, an explanation of the biological or mechanistic rationale behind the ability of the 80S ribosome to cause upstream 40S ribosomes to dissociate from mRNA would help clarify this aspect of the model.

Thank you for this suggestion. In the original submission, we described our modifications to the ICIER model in the section titled “An extended ICIER model for quantifying uORF buffering in CDS translation” (Lines 88-124 of the revised manuscript). 

To further clarify the biological rationale behind this mechanism, we have now included a conceptual model figure (Figure 9) illustrating mechanistically how uORF translation can buffer downstream translation within a single mRNA molecule. Additionally, we expanded the Discussion to summarize the current understanding of how collisions between translating 80S ribosomes and scanning 40S subunits may lead to dissociation, referencing known initial ribosome quality control (iRQC) pathways. These revisions provide a clearer mechanistic framework for interpreting the buffering effects modeled in our simulations. The relevant part is reproduced from Discussion (Lines 540-557) which reads as follows:

“Ribosome slowdown or stalling on mRNA due to rare codons [56,96-98] or nascent blocking peptides [99-102] frequently triggers ribosome collisions genome-wide [103-105]. Such collisions, especially among elongating 80S ribosomes, often activate ribosome quality control (RQC) pathways that recognize collision interfaces on the 40S subunit, leading to ribosomal subunit dissociation and degradation [106-108]. In mammals, ZNF598 specifically identifies collided ribosomes to initiate ubiquitin-dependent protein and mRNA quality control pathways [109-113]. Analogously, yeast employs Hel2-mediated ubiquitination of uS10, initiating dissociation via the RQC-trigger complex (RQT) [114]. Furthermore, the human RQT (hRQT) complex recognizes ubiquitinated ribosomes and induces subunit dissociation similarly to yeast RQT [115]. However, transient ribosome collisions can evade RQC by promoting resumed elongation through mechanical force provided by trailing ribosomes, thereby mitigating stalling [116]. Beyond 80S collisions, evidence increasingly highlights a distinct collision type involving scanning 40S subunits or pre-initiation (43S) complexes. Recently, an initiation RQC pathway (iRQC) targeting the small ribosomal subunit (40S) has been described, particularly involving collisions between scanning 43S complexes or between stalled 43S and elongating 80S ribosomes (Figure 9B) [117,118]. During iRQC, E3 ubiquitin ligase RNF10 ubiquitinates uS3 and uS5 proteins, resulting in 40S degradation [118]. This mechanism aligns closely with our ICIER model, proposing collision-driven 43S dissociation in the 5' UTRs. Future studies exploring these mechanisms in greater detail will clarify how uORFs modulate translational regulation through buffering effects.”

(2) The figure legend references Figure 5C; however, this figure appears to be missing from the document.

We apologize for the oversight. The missing panel previously referred to as Figure 5C has now been incorporated into the revised Figure 6A. The figure and its corresponding legend have been corrected accordingly in the updated manuscript.

Reviewer #2 (Recommendations for the authors):

This is an important study that enhances our understanding of the roles of uORFs in translational regulation. In addition to the suggestions provided in the public review, the following minor points should be addressed before publication in eLife:

(1) Page 7, line 207: "We identified 18,412 canonical uORFs shared between the two species (referred to as conserved uORFs hereafter)." The term "canonical uORFs" requires clarification. Does this refer to uORFs with specific sequence features, conservation, or another defining characteristic?

Thank you for pointing this out. We apologize for the lack of clarity. In our study, a canonical uORF is defined as an open reading frame (ORF) that initiates with a canonical AUG start codon located in the 5′ untranslated region (UTR) and terminates with a stop codon (UAA, UAG, or UGA) within the same mRNA. Conservation of uORFs is defined solely based on the presence of AUG start codons at orthologous positions in the 5′ UTR across species, regardless of differences in the stop codon.

To clarify this definition, we have revised the sentence as follows (Lines 213-219): “We focused on canonical uORFs that initiate with an ATG start codon in the 5′ UTR and terminate with a stop codon (TAA, TAG, or TGA). Because the ATG start codon is the defining feature of a canonical uORF and tends to be more conserved than its downstream sequence [67], we defined uORF conservation based on the presence of the ATG start codon in the 5′ UTR of D. melanogaster and its orthologous positions in D. simulans, regardless of differences in the stop codon. Using this criterion, we identified 18,412 canonical uORFs with conserved start codons between the two species.”

(2) Page 8, line 227: "Furthermore, the dominant uORFs showed a higher proportion of conserved uATGs than the other translated uORFs." There appears to be a typographical error. Should "other uATGs" instead read "other uORFs"?

Thank you for pointing this out. As we addressed in response to your previous concern, in this study, we defined uORF conservation primarily based on the presence of their start codon (uATG) both in D. melanogaster and the orthologous sites of D. simulans, as the start codon is the defining feature of a uORF and tends to be more conserved than the remaining sequence, as demonstrated in our previous study [7]. We used the term “conserved uATGs” to reflect this definition and believe it accurately conveys the intended meaning in this context.

(3) Page 8, line 240: "uORFs exhibited a significant positive correlation with the TE of their downstream CDSs in all samples analyzed (P < 0.001, Spearman's correlation)." A Spearman's rho of 0.11 or 0.21 may not practically represent a "significant" positive correlation. Consider rephrasing this as "a positive correlation."

Thank you for the suggestion. We have revised the sentence in the manuscript to read (Lines 257-259): “uORFs exhibited a modest, yet statistically significant, positive correlation with the TE of their downstream CDSs across all samples analyzed (P < 0.001, Spearman’s correlation).”

(4) Page 9, line 269: The analysis of interspecific TE changes between uORFs and their corresponding CDSs is a crucial piece of evidence supporting the authors' conclusions. Presenting this analysis as part of the figures, rather than in "Table 1," would improve clarity and accessibility.

Thank you for this suggestion. In Table 1, we originally presented the number of uORFs and CDSs that showed significant differences in TE between D. melanogaster and D. simulans during various developmental stages. One key point we aimed to emphasize was that, although TE changes in uORFs and their downstream CDSs are positively correlated, there is a notable difference in the magnitude of these changes. To better convey this, we have summarized the core findings of Table 1 in graphical form.

In Figure 3B of the revised version, we compared the absolute values of interspecific TE changes between CDS and uORF, showing that CDSs consistently exhibit smaller shifts than their upstream uORFs. This result further supports the translational buffering effect of uORFs on downstream CDS expression. We have included the updated results in the revised manuscript (Lines 281-284) as follows:

“In fact, the absolute values of log2(fold change) of TE for uORFs between D. melanogaster and D. simulans was significantly greater than that observed for corresponding CDSs across all samples (P < 0.001, Wilcoxon signed-rank test; Figure 3B), suggesting that the magnitude of TE changes in CDSs is generally smaller than that in uORFs, due to the buffering effect of uORF.”

(5) Page 9, line 279: The phrase "dominantly translated" needs clarification. Does it refer to Figure 2C, where one uORF is dominantly translated within a gene, or does it mean that the uORF's translation is higher than that of its corresponding CDS?

We apologize for the obscurity. The phrase "dominantly translated" means one uORF with the highest TE compared to other uORFs within a gene. We have rephrased the relevant sentence in the revised version (Lines 299-304), which now reads:

“To investigate how the conservation level and translation patterns of uORFs influence their buffering capacity on CDS translation, we categorized genes expressed in each pair of samples into three classes:

Class I, genes with conserved uORFs that are dominantly translated (i.e., exhibiting the highest TE among all uORFs within the same gene) in both Drosophila species; Class II, genes with conserved uORFs that are translated in both species but not dominantly translated in at least one; and Class III, the remaining expressed genes.”

(6) The sequencing data and analysis code should be made publicly available before publication to ensure transparency and reproducibility.

Thank you for this suggestion. As described in the Data availability section, all deepsequencing data generated in this study, including single-ended mRNA-Seq and Ribo-Seq data of 10 developmental stages and tissues of Drosophila simulans and paired-end mRNA-Seq data of 0-2 h, 26 h, 6-12 h, and 12-24 h Drosophila melanogaster embryos, were deposited in the China National Genomics Data Center Genome Sequence Archive (GSA) under accession numbers CRA003198, CRA007425, and CRA007426. The mRNA-Seq and Ribo-Seq data for the different developmental stages and tissues of Drosophila melanogaster were published in our previous paper [8] and were deposited in the Sequence Read Archive (SRA) under accession number SRP067542.

All original code has been deposited on GitHub: https://github.com/lujlab/uORF_buffer; https://github.com/lujlab/Buffer_eLife2025.

Response reference

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