Author response:

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

Reviewer #1 (Public review):

Summary:

From a forward genetic mosaic mutant screen using EMS, the authors identify mutations in glucosylceramide synthase (GlcT), a rate-limiting enzyme for glycosphingolipid (GSL) production, that result in EE tumors. Multiple genetic experiments strongly support the model that the mutant phenotype caused by GlcT loss is due to by failure of conversion of ceramide into glucosylceramide. Further genetic evidence suggests that Notch signaling is comprised in the ISC lineage and may affect the endocytosis of Delta. Loss of GlcT does not affect wing development or oogenesis, suggesting tissue-specific roles for GlcT. Finally, an increase in goblet cells in UGCG knockout mice, not previously reported, suggests a conserved role for GlcT in Notch signaling in intestinal cell lineage specification.

Strengths:

Overall, this is a well-written paper with multiple well-designed and executed genetic experiments that support a role for GlcT in Notch signaling in the fly and mammalian intestine. I do, however, have a few comments below.

Weaknesses:

(1) The authors bring up the intriguing idea that GlcT could be a way to link diet to cell fate choice. Unfortunately, there are no experiments to test this hypothesis.

We indeed attempted to establish an assay to investigate the impact of various diets (such as high-fat, high-sugar, or high-protein diets) on the fate choice of ISCs. Subsequently, we intended to examine the potential involvement of GlcT in this process. However, we observed that the number or percentage of EEs varies significantly among individuals, even among flies with identical phenotypes subjected to the same nutritional regimen. We suspect that the proliferative status of ISCs and the turnover rate of EEs may significantly influence the number of EEs present in the intestinal epithelium, complicating the interpretation of our results. Consequently, we are unable to conduct this experiment at this time. The hypothesis suggesting that GlcT may link diet to cell fate choice remains an avenue for future experimental exploration.

(2) Why do the authors think that UCCG knockout results in goblet cell excess and not in the other secretory cell types?

This is indeed an interesting point. In the mouse intestine, it is well-documented that the knockout of Notch receptors or Delta-like ligands results in a classic phenotype characterized by goblet cell hyperplasia, with little impact on the other secretory cell types. This finding aligns very well with our experimental results, as we noted that the numbers of Paneth cells and enteroendocrine cells appear to be largely normal in UGCG knockout mice. By contrast, increases in other secretory cell types are typically observed under conditions of pharmacological inhibition of the Notch pathway.

(3) The authors should cite other EMS mutagenesis screens done in the fly intestine.

To our knowledge, the EMS screen on 2L chromosome conducted in Allison Bardin’s lab is the only one prior to this work, which leads to two publications (Perdigoto et al., 2011; Gervais, et al., 2019). We have now included citations for both papers in the revised manuscript.

(4) The absence of a phenotype using NRE-Gal4 is not convincing. This is because the delay in its expression could be after the requirement for the affected gene in the process being studied. In other words, sufficient knockdown of GlcT by RNA would not be achieved until after the relevant signaling between the EB and the ISC occurred. Dl-Gal4 is problematic as an ISC driver because Dl is expressed in the EEP.

This is an excellent point, and we agree that the lack of an observable phenotype using NRE-Gal4 could be due to delayed expression, which may result in missing the critical window required for effective GlcT knockdown. Consequently, we cannot rule out the possibility that GlcT also plays a role in early EBs or EEPs. We have revised the manuscript to soften this conclusion and to include this alternative explanation for the experiment.

(5) The difference in Rab5 between control and GlcT-IR was not that significant. Furthermore, any changes could be secondary to increases in proliferation.

We agree that it is possible that the observed increase in proliferation could influence the number of Rab5+ endosomes, and we will temper our conclusions on this aspect accordingly. However, it is important to note that, although the difference in Rab5+ endosomes between the control and GlcT-IR conditions appeared mild, it was statistically significant and reproducible. In our revised experiments, we have not only added statistical data and immunofluorescence images for Rab11 but also unified the approaches used for detecting Rab-associated proteins (in the previous figures, Rab5 was shown using U-Rab5-GFP, whereas Rab7 was detected by direct antibody staining). Based on this unified strategy, we optimized the quantification of Dl-GFP colocalization with early, late, and recycling endosomes, and the results are consistent with our previous observations (see the updated Fig. 5).

Reviewer #2 (Public review):

Summary:

This study genetically identifies two key enzymes involved in the biosynthesis of glycosphingolipids, GlcT and Egh, which act as tumor suppressors in the adult fly gut. Detailed genetic analysis indicates that a deficiency in Mactosyl-ceramide (Mac-Cer) is causing tumor formation. Analysis of a Notch transcriptional reporter further indicates that the lack of Mac-Ser is associated with reduced Notch activity in the gut, but not in other tissues.

Addressing how a change in the lipid composition of the membranes might lead to defective Notch receptor activation, the authors studied the endocytic trafficking of Delta and claimed that internalized Delta appeared to accumulate faster into endosomes in the absence of Mac-Cer. Further analysis of Delta steady-state accumulation in fixed samples suggested a delay in the endosomal trafficking of Delta from Rab5+ to Rab7+ endosomes, which was interpreted to suggest that the inefficient, or delayed, recycling of Delta might cause a loss in Notch receptor activation.

Finally, the histological analysis of mouse guts following the conditional knock-out of the GlcT gene suggested that Mac-Cer might also be important for proper Notch signaling activity in that context.

Strengths:

The genetic analysis is of high quality. The finding that a Mac-Cer deficiency results in reduced Notch activity in the fly gut is important and fully convincing.

The mouse data, although preliminary, raised the possibility that the role of this specific lipid may be conserved across species.

Weaknesses:

This study is not, however, without caveats and several specific conclusions are not fully convincing.

First, the conclusion that GlcT is specifically required in Intestinal Stem Cells (ISCs) is not fully convincing for technical reasons: NRE-Gal4 may be less active in GlcT mutant cells, and the knock-down of GlcT using Dl-Gal4ts may not be restricted to ISCs given the perdurance of Gal4 and of its downstream RNAi.

As previously mentioned, we acknowledge that a role for GlcT in early EBs or EEPs cannot be completely ruled out. We have revised our manuscript to present a more cautious conclusion and explicitly described this possibility in the updated version.

Second, the results from the antibody uptake assays are not clear.: i) the levels of internalized Delta were not quantified in these experiments; ii) additionally, live guts were incubated with anti-Delta for 3hr. This long period of incubation indicated that the observed results may not necessarily reflect the dynamics of endocytosis of antibody-bound Delta, but might also inform about the distribution of intracellular Delta following the internalization of unbound anti-Delta. It would thus be interesting to examine the level of internalized Delta in experiments with shorter incubation time.

We thank the reviewer for these excellent questions. In our antibody uptake experiments, we noted that Dl reached its peak accumulation after a 3-hour incubation period. We recognize that quantifying internalized Dl would enhance our analysis, and we will include the corresponding statistical graphs in the revised version of the manuscript. In addition, we agree that during the 3-hour incubation, the potential internalization of unbound anti-Dl cannot be ruled out, as it may influence the observed distribution of intracellular Dl. We therefore attempted to supplement our findings with live imaging experiments to investigate the dynamics of Dl/Notch endocytosis in both normal and GlcT mutant ISCs. However, we found that the GFP expression level of Dl-GFP (either in the knock-in or transgenic line) was too low to be reliably tracked. During the three-hour observation period, the weak GFP signal remained largely unchanged regardless of the GlcT mutation status, and the signal resolution under the microscope was insufficient to clearly distinguish membrane-associated from intracellular Dl. Therefore, we were unable to obtain a dynamic view of Dl trafficking through live imaging. Nevertheless, our Dl antibody uptake and endosomal retention analyses collectively support the notion that MacCer influences Notch signaling by regulating Dl endocytosis.

Overall, the proposed working model needs to be solidified as important questions remain open, including: is the endo-lysosomal system, i.e. steady-state distribution of endo-lysosomal markers, affected by the Mac-Cer deficiency? Is the trafficking of Notch also affected by the Mac-Cer deficiency? is the rate of Delta endocytosis also affected by the Mac-Cer deficiency? are the levels of cell-surface Delta reduced upon the loss of Mac-Cer?

Regarding the impact on the endo-lysosomal system, this is indeed an important aspect to explore. While we did not conduct experiments specifically designed to evaluate the steady-state distribution of endo-lysosomal markers, our analyses utilizing Rab5-GFP overexpression and Rab7 staining did not indicate any significant differences in endosome distribution in MacCer deficient conditions. Moreover, we still observed high expression of the NRE-LacZ reporter specifically at the boundaries of clones in GlcT mutant cells (Fig. 4A), indicating that GlcT mutant EBs remain responsive to Dl produced by normal ISCs located right at the clone boundary. Therefore, we propose that MacCer deficiency may specifically affect Dl trafficking without impacting Notch trafficking.

In our 3-hour antibody uptake experiments, we observed a notable decrease in cell-surface Dl, which was accompanied by an increase in intracellular accumulation. These findings collectively suggest that Dl may be unstable on the cell surface, leading to its accumulation in early endosomes.

Third, while the mouse results are potentially interesting, they seem to be relatively preliminary, and future studies are needed to test whether the level of Notch receptor activation is reduced in this model.

In the mouse small intestine, Olfm4 is a well-established target gene of the Notch signaling pathway, and its staining provides a reliable indication of Notch pathway activation. While we attempted to evaluate Notch activation using additional markers, such as Hes1 and NICD, we encountered difficulties, as the corresponding antibody reagents did not perform well in our hands. Despite these challenges, we believe that our findings with Olfm4 provide an important start point for further investigation in the future.

Reviewer #3 (Public review):

Summary:

In this paper, Tang et al report the discovery of a Glycoslyceramide synthase gene, GlcT, which they found in a genetic screen for mutations that generate tumorous growth of stem cells in the gut of Drosophila. The screen was expertly done using a classic mutagenesis/mosaic method. Their initial characterization of the GlcT alleles, which generate endocrine tumors much like mutations in the Notch signaling pathway, is also very nice. Tang et al checked other enzymes in the glycosylceramide pathway and found that the loss of one gene just downstream of GlcT (Egh) gives similar phenotypes to GlcT, whereas three genes further downstream do not replicate the phenotype. Remarkably, dietary supplementation with a predicted GlcT/Egh product, Lactosyl-ceramide, was able to substantially rescue the GlcT mutant phenotype. Based on the phenotypic similarity of the GlcT and Notch phenotypes, the authors show that activated Notch is epistatic to GlcT mutations, suppressing the endocrine tumor phenotype and that GlcT mutant clones have reduced Notch signaling activity. Up to this point, the results are all clear, interesting, and significant. Tang et al then go on to investigate how GlcT mutations might affect Notch signaling, and present results suggesting that GlcT mutation might impair the normal endocytic trafficking of Delta, the Notch ligand. These results (Fig X-XX), unfortunately, are less than convincing; either more conclusive data should be brought to support the Delta trafficking model, or the authors should limit their conclusions regarding how GlcT loss impairs Notch signaling. Given the results shown, it's clear that GlcT affects EE cell differentiation, but whether this is via directly altering Dl/N signaling is not so clear, and other mechanisms could be involved. Overall the paper is an interesting, novel study, but it lacks somewhat in providing mechanistic insight. With conscientious revisions, this could be addressed. We list below specific points that Tang et al should consider as they revise their paper.

Strengths:

The genetic screen is excellent.

The basic characterization of GlcT phenotypes is excellent, as is the downstream pathway analysis.

Weaknesses:

(1) Lines 147-149, Figure 2E: here, the study would benefit from quantitations of the effects of loss of brn, B4GalNAcTA, and a4GT1, even though they appear negative.

We have incorporated the quantifications for the effects of the loss of brn, B4GalNAcTA, and a4GT1 in the updated Figure 2.

(2) In Figure 3, it would be useful to quantify the effects of LacCer on proliferation. The suppression result is very nice, but only effects on Pros+ cell numbers are shown.

We have now added quantifications of the number of EEs per clone to the updated Figure 3.

(3) In Figure 4A/B we see less NRE-LacZ in GlcT mutant clones. Are the data points in Figure 4B per cell or per clone? Please note. Also, there are clearly a few NRE-LacZ+ cells in the mutant clone. How does this happen if GlcT is required for Dl/N signaling?

In Figure 4B, the data points represent the fluorescence intensity per single cell within each clone. It is true that a few NRE-LacZ+ cells can still be observed within the mutant clone; however, this does not contradict our conclusion. As noted, high expression of the NRE-LacZ reporter was specifically observed around the clone boundaries in MacCer deficient cells (Fig. 4A), indicating that the mutant EBs can normally receive Dl signal from the normal ISCs located at the clone boundary and activate the Notch signaling pathway. Therefore, we believe that, although affecting Dl trafficking, MacCer deficiency does not significantly affect Notch trafficking.

(4) Lines 222-225, Figure 5AB: The authors use the NRE-Gal4ts driver to show that GlcT depletion in EBs has no effect. However, this driver is not activated until well into the process of EB commitment, and RNAi's take several days to work, and so the author's conclusion is "specifically required in ISCs" and not at all in EBs may be erroneous.

As previously mentioned, we acknowledge that a role for GlcT in early EBs or EEPs cannot be completely ruled out. We have revised our manuscript to present a more cautious conclusion and described this possibility in the updated version.

(5) Figure 5C-F: These results relating to Delta endocytosis are not convincing. The data in Fig 5C are not clear and not quantitated, and the data in Figure 5F are so widely scattered that it seems these co-localizations are difficult to measure. The authors should either remove these data, improve them, or soften the conclusions taken from them. Moreover, it is unclear how the experiments tracing Delta internalization (Fig 5C) could actually work. This is because for this method to work, the anti-Dl antibody would have to pass through the visceral muscle before binding Dl on the ISC cell surface. To my knowledge, antibody transcytosis is not a common phenomenon.

We thank the reviewer for these insightful comments and suggestions. In our in vivo experiments, we observed increased co-localization of Rab5 and Dl in GlcT mutant ISCs, indicating that Dl trafficking is delayed at the transition to Rab7⁺ late endosomes, a finding that is further supported by our antibody uptake experiments. We acknowledge that the data presented in Fig. 5C are not fully quantified and that the co-localization data in Fig. 5F may appear somewhat scattered; therefore, we have included additional quantification and enhanced the data presentation in the revised manuscript.

Regarding the concern about antibody internalization, we appreciate this point. We currently do not know if the antibody reaches the cell surface of ISCs by passing through the visceral muscle or via other routes. Given that the experiment was conducted with fragmented gut, it is possible that the antibody may penetrate into the tissue through mechanisms independent of transcytosis.

As mentioned earlier, we attempted to supplement our findings with live imaging experiments to investigate the dynamics of Dl/Notch endocytosis in both normal and GlcT mutant ISCs. However, we found that the GFP expression level of Dl-GFP (either in the knock-in or transgenic line) was too low to be reliably tracked. During the three-hour observation period, the weak GFP signal remained largely unchanged regardless of the GlcT mutation status, and the signal resolution under the microscope was insufficient to clearly distinguish membrane-associated from intracellular Dl. Therefore, we were unable to obtain a dynamic view of Dl trafficking through live imaging. Nevertheless, our Dl antibody uptake and endosomal retention analyses collectively support the notion that MacCer influences Notch signaling by regulating Dl endocytosis.

(6) It is unclear whether MacCer regulates Dl-Notch signaling by modifying Dl directly or by influencing the general endocytic recycling pathway. The authors say they observe increased Dl accumulation in Rab5+ early endosomes but not in Rab7+ late endosomes upon GlcT depletion, suggesting that the recycling endosome pathway, which retrieves Dl back to the cell surface, may be impaired by GlcT loss. To test this, the authors could examine whether recycling endosomes (marked by Rab4 and Rab11) are disrupted in GlcT mutants. Rab11 has been shown to be essential for recycling endosome function in fly ISCs.

We agree that assessing the state of recycling endosomes, especially by using markers such as Rab11, would be valuable in determining whether MacCer regulates Dl-Notch signaling by directly modifying Dl or by influencing the broader endocytic recycling pathway. In the newly added experiments, we found that in GlcT-IR flies, Dl still exhibits partial colocalization with Rab11, and the overall expression pattern of Rab11 is not affected by GlcT knockdown (Fig. 5E-F). These observations suggest that MacCer specifically regulates Dl trafficking rather than broadly affecting the recycling pathway.

(7) It remains unclear whether Dl undergoes post-translational modification by MacCer in the fly gut. At a minimum, the authors should provide biochemical evidence (e.g., Western blot) to determine whether GlcT depletion alters the protein size of Dl.

While we propose that MacCer may function as a component of lipid rafts, facilitating Dl membrane anchorage and endocytosis, we also acknowledge the possibility that MacCer could serve as a substrate for protein modifications of Dl necessary for its proper function. Conducting biochemical analyses to investigate potential post-translational modifications of Dl by MacCer would indeed provide valuable insights. We have performed Western blot analysis to test whether GlcT depletion affects the protein size of Dl. As shown below, we did not detect any apparent changes in the molecular weight of the Dl protein. Therefore, it is unlikely that MacCer regulates post-translational modifications of Dl.

Author response image 1.

To investigate whether MacCer modifies Dl by Western blot,(A) Four lanes were loaded: the first two contained 20 μL of membrane extract (lane 1: GlcT-IR, lane 2: control), while the last two contained 10 μL of membrane extract (B) Full blot images are shown under both long and shortexposure conditions.

(8) It is unfortunate that GlcT doesn't affect Notch signaling in other organs on the fly. This brings into question the Delta trafficking model and the authors should note this. Also, the clonal marker in Figure 6C is not clear.

In the revised working model, we have explicitly described that the events occur in intestinal stem cells. Regarding Figure 6C, we have delineated the clone with a white dashed line to enhance its clarity and visual comprehension.

(9) The authors state that loss of UGCG in the mouse small intestine results in a reduced ISC count. However, in Supplementary Figure C3, Ki67, a marker of ISC proliferation, is significantly increased in UGCG-CKO mice. This contradiction should be clarified. The authors might repeat this experiment using an alternative ISC marker, such as Lgr5.

Previous studies have indicated that dysregulation of the Notch signaling pathway can result in a reduction in the number of ISCs. While we did not perform a direct quantification of ISC numbers in our experiments, our Olfm4 staining—which serves as a reliable marker for ISCs—demonstrates a clear reduction in the number of positive cells in UGCG-CKO mice.

The increased Ki67 signal we observed reflects enhanced proliferation in the transit-amplifying region, and it does not directly indicate an increase in ISC number. Therefore, in UGCG-CKO mice, we observe a decrease in the number of ISCs, while there is an increase in transit-amplifying (TA) cells (progenitor cells). This increase in TA cells is probably a secondary consequence of the loss of barrier function associated with the UGCG knockout.

Author response:

Public Reviews:

Reviewer #1 (Public review):

The study analyzes the gastric fluid DNA content identified as a potential biomarker for human gastric cancer. However, the study lacks overall logicality, and several key issues require improvement and clarification. In the opinion of this reviewer, some major revisions are needed:

(1) This manuscript lacks a comparison of gastric cancer patients' stages with PN and N+PD patients, especially T0-T2 patients.

We are grateful for this astute remark. A comparison of gfDNA concentration among the diagnostic groups indicates a trend of increasing values as the diagnosis progresses toward malignancy. The observed values for the diagnostic groups are as follows:

Author response table 1.

The chart below presents the statistical analyses of the same diagnostic/tumor-stage groups (One-Way ANOVA followed by Tukey’s multiple comparison tests). It shows that gastric fluid gfDNA concentrations gradually increase with malignant progression. We observed that the initial tumor stages (T0 to T2) exhibit intermediate gfDNA levels, which in this group is significantly lower than in advanced disease (p = 0.0036), but not statistically different from non-neoplastic disease (p = 0.74).

Author response image 1.

(2) The comparison between gastric cancer stages seems only to reveal the difference between T3 patients and early-stage gastric cancer patients, which raises doubts about the authenticity of the previous differences between gastric cancer patients and normal patients, whether it is only due to the higher number of T3 patients.

We appreciate the attention to detail regarding the numbers analyzed in the manuscript. Importantly, the results are meaningful because the number of subjects in each group is comparable (T0-T2, N = 65; T3, N = 91; T4, N = 63). The mean gastric fluid gfDNA values (ng/µL) increase with disease stage (T0-T2: 15.12; T3-T4: 30.75), and both are higher than the mean gfDNA values observed in non-neoplastic disease (10.81 ng/µL for N+PD and 10.10 ng/µL for PN). These subject numbers in each diagnostic group accurately reflect real-world data from a tertiary cancer center.

(3) The prognosis evaluation is too simplistic, only considering staging factors, without taking into account other factors such as tumor pathology and the time from onset to tumor detection.

Histopathological analyses were performed throughout the study not only for the initial diagnosis of tissue biopsies, but also for the classification of Lauren’s subtypes, tumor staging, and the assessment of the presence and extent of immune cell infiltrates. Regarding the time of disease onset, this variable is inherently unknown--by definition--at the time of a diagnostic EGD. While the prognosis definition is indeed straightforward, we believe that a simple, cost-effective, and practical approach is advantageous for patients across diverse clinical settings and is more likely to be effectively integrated into routine EGD practice.

(4) The comparison between gfDNA and conventional pathological examination methods should be mentioned, reflecting advantages such as accuracy and patient comfort.

We wish to reinforce that EGD, along with conventional histopathology, remains the gold standard for gastric cancer evaluation. EGD under sedation is routinely performed for diagnosis, and the collection of gastric fluids for gfDNA evaluation does not affect patient comfort. Thus, while gfDNA analysis was evidently not intended as a diagnostic EGD and biopsy replacement, it may provide added prognostic value to this exam.

(5) There are many questions in the figures and tables. Please match the Title, Figure legends, Footnote, Alphabetic order, etc.

We are grateful for these comments and apologize for the clerical oversight. All figures, tables, titles and figure legends have now been double-checked.

(6) The overall logicality of the manuscript is not rigorous enough, with few discussion factors, and cannot represent the conclusions drawn.

We assume that the unusual wording remark regarding “overall logicality” pertains to the rationale and/or reasoning of this investigational study. Our working hypothesis was that during neoplastic disease progression, tumor cells continuously proliferate and, depending on various factors, attract immune cell infiltrates. Consequently, both tumor cells and immune cells (as well as tumor-derived DNA) are released into the fluids surrounding the tumor at its various locations, including blood, urine, saliva, gastric fluids, and others. Thus, increases in DNA levels within some of these fluids have been documented and are clinically meaningful. The concurrent observation of elevated gastric fluid gfDNA levels and immune cell infiltration supports the hypothesis that increased gfDNA—which may originate not only from tumor cells but also from immune cells—could be associated with better prognosis, as suggested by this study of a large real-world patient cohort.

In summary, we thank Reviewer #1 for his time and effort in a constructive critique of our work.

Reviewer #2 (Public review):

Summary:

The authors investigated whether the total DNA concentration in gastric fluid (gfDNA), collected via routine esophagogastroduodenoscopy (EGD), could serve as a diagnostic and prognostic biomarker for gastric cancer. In a large patient cohort (initial n=1,056; analyzed n=941), they found that gfDNA levels were significantly higher in gastric cancer patients compared to non-cancer, gastritis, and precancerous lesion groups. Unexpectedly, higher gfDNA concentrations were also significantly associated with better survival prognosis and positively correlated with immune cell infiltration. The authors proposed that gfDNA may reflect both tumor burden and immune activity, potentially serving as a cost-effective and convenient liquid biopsy tool to assist in gastric cancer diagnosis, staging, and follow-up.

Strengths:

This study is supported by a robust sample size (n=941) with clear patient classification, enabling reliable statistical analysis. It employs a simple, low-threshold method for measuring total gfDNA, making it suitable for large-scale clinical use. Clinical confounders, including age, sex, BMI, gastric fluid pH, and PPI use, were systematically controlled. The findings demonstrate both diagnostic and prognostic value of gfDNA, as its concentration can help distinguish gastric cancer patients and correlates with tumor progression and survival. Additionally, preliminary mechanistic data reveal a significant association between elevated gfDNA levels and increased immune cell infiltration in tumors (p=0.001).

Reviewer #2 has conceptually grasped the overall rationale of the study quite well, and we are grateful for their assessment and comprehensive summary of our findings.

Weaknesses:

(1) The study has several notable weaknesses. The association between high gfDNA levels and better survival contradicts conventional expectations and raises concerns about the biological interpretation of the findings.

We agree that this would be the case if the gfDNA was derived solely from tumor cells. However, the findings presented here suggest that a fraction of this DNA would be indeed derived from infiltrating immune cells. The precise determination of the origin of this increased gfDNA remains to be achieved in future follow-up studies, and these are planned to be evaluated soon, by applying DNA- and RNA-sequencing methodologies and deconvolution analyses.

(2) The diagnostic performance of gfDNA alone was only moderate, and the study did not explore potential improvements through combination with established biomarkers. Methodological limitations include a lack of control for pre-analytical variables, the absence of longitudinal data, and imbalanced group sizes, which may affect the robustness and generalizability of the results.

Reviewer #2 is correct that this investigational study was not designed to assess the diagnostic potential of gfDNA. Instead, its primary contribution is to provide useful prognostic information. In this regard, we have not yet explored combining gfDNA with other clinically well-established diagnostic biomarkers. We do acknowledge this current limitation as a logical follow-up that must be investigated in the near future.

Moreover, we collected a substantial number of pre-analytical variables within the limitations of a study involving over 1,000 subjects. Longitudinal samples and data were not analyzed here, as our aim was to evaluate prognostic value at diagnosis. Although the groups are imbalanced, this accurately reflects the real-world population of a large endoscopy center within a dedicated cancer facility. Subjects were invited to participate and enter the study before sedation for the diagnostic EGD procedure; thus, samples were collected prospectively from all consenting individuals.

Finally, to maintain a large, unbiased cohort, we did not attempt to balance the groups, allowing analysis of samples and data from all patients with compatible diagnoses (please see Results: Patient groups and diagnoses).

(3) Additionally, key methodological details were insufficiently reported, and the ROC analysis lacked comprehensive performance metrics, limiting the study's clinical applicability.

We are grateful for this useful suggestion. In the current version, each ROC curve (Supplementary Figures 1A and 1B) now includes the top 10 gfDNA thresholds, along with their corresponding sensitivity and specificity values (please see Suppl. Table 1). The thresholds are ordered from-best-to-worst based on the classic Youden’s J statistic, as follows:

Youden Index = specificity + sensitivity – 1 [Youden WJ. Index for rating diagnostic tests. Cancer 3:32-35, 1950. PMID: 15405679]. We have made an effort to provide all the key methodological details requested, but we would be glad to add further information upon specific request.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #3 (Recommendations for the authors):

The authors have done an excellent job of addressing most comments, but my concerns about Figure 5 remain. I appreciate the authors' efforts to address the problem involving Rs being part of the computation on both the x and y axes of Figure 5, but addressing this via simulation addresses statistical significance but overlooks effect size. I think the authors may have misunderstood my original suggestion, so I will attempt to explain it better here. Since "Rs" is an average across all trials, the trials could be subdivided in two halves to compute two separate averages - for example, an average of the even numbered trials and an average of the odd numbered trials. Then you would use the "Rs" from the even numbered trials for one axis and the "Rs" from the odd numbered trials for the other. You would then plot R-Rs_even vs Rf-Rs_odd. This would remove the confound from this figure, and allow the text/interpretation to be largely unchanged (assuming the results continue to look as they do).

We have added a description and the result of the new analysis (line #321 to #332), and a supplementary figure (Suppl. Fig. 1) (line #1464 to #1477). 

“We calculated 𝑅_𝑠 in the ordinate and abscissa of Figure 5A-E using responses averaged across different subsets of trials, such that 𝑅_𝑠 was no longer a common term in the ordinate and abscissa. For each neuron, we determined 𝑅_𝑠1 by averaging the firing rates of 𝑅_𝑠 across half of the recorded trials, selected randomly. We also determined 𝑅_𝑠2 by averaging the firing rates of 𝑅_𝑠 across the rest of the trials.  We regressed (𝑅 − 𝑅_𝑠1 )  on (𝑅_𝑓 − 𝑅_𝑠2) , as well as (𝑅_𝑠 - 𝑅_𝑠2)  on (𝑅_𝑓 − 𝑅_𝑠1), and repeated the procedure 50 times. The averaged slopes obtained with 𝑅_𝑠 from the split trials showed the same pattern as those using 𝑅_𝑠 from all trials (Table 1 and Supplementary Fig. 1), although the coefficient of determination was slightly reduced (Table 1). For ×4 speed separation, the slopes were nearly identical to those shown in Figure 5F1. For ×2 speed separation, the slopes were slightly smaller than those in Figure 5F2, but followed the same pattern (Supplementary Fig. 1). Together, these analysis results confirmed the faster-speed bias at the slow stimulus speeds, and the change of the response weights as stimulus speeds increased.”

An additional remaining item concerns the terminology weighted sum, in the context of the constraint that wf and ws must sum to one. My opinion is that it is non-standard to use weighted sum when the computation is a weighted average, but as long as the authors make their meaning clear, the reader will be able to follow. I suggest adding some phrasing to explain to the reader the shift in interpretation from the more general weighted sum to the more constrained weighted average. Specifically, "weighted sum" first appears on line 268, and then the additional constraint of ws + wf =1 is introduced on line 278. Somewhere around line 278, it would be useful to include a sentence stating that this constraint means the weighted sum is constrained to be a weighted average.

Thanks for the suggestion. We have modified the text as follows. Since we made other modifications in the text, the line numbers are slightly different from the last version. 

Line #274 to 275: 

“Since it is not possible to solve for both variables, 𝑤_𝑠 and 𝑤_𝑓, from a single equation (Eq. 5) with three data points, we introduced an additional constraint: 𝑤_𝑠 + 𝑤_𝑓 =1. With this constraint, the weighted sum becomes a weighted average.”

Also on line #309:

“First, at each speed pair and for each of the 100 neurons in the data sample shown in Figure 5, we simulated the response to the bi-speed stimuli (𝑅_𝑒) as a randomly weighted average of 𝑅_𝑓 and 𝑅_𝑠 of the same neuron. 

in which 𝑎 was a randomly generated weight (between 0 and 1) for 𝑅_𝑓, and the weights for 𝑅_𝑓 and 𝑅_𝑠 summed to one.”

Author response:

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

Reviewer #1 (Public review):

The authors focus on the molecular mechanisms by which EMT cells confer resistance to cancer cells. The authors use a wide range of methods to reveal that overexpression of Snail in EMT cells induces cholesterol/sphingomyelin imbalance via transcriptional repression of biosynthetic enzymes involved in sphingomyelin synthesis. The study also revealed that ABCA1 is important for cholesterol efflux and thus for counterbalancing the excess of intracellular free cholesterol in these snail-EMT cells. Inhibition of ACAT, an enzyme catalyzing cholesterol esterification, also seems essential to inhibit the growth of snail-expressing cancer cells.

However, It seems important to analyze the localization of ABCA1, as it is possible that in the event of cholesterol/sphingomyelin imbalance, for example, the intracellular trafficking of the pump may be altered.

The authors should also analyze ACAT levels and/or activity in snail-EMT cells that should be increased. Overall, the provided data are important to better understand cancer biology.

We thank the reviewer for recognizing the significance of our study. Consistent with the hypothesis that ABCA1 contributes to chemoresistance in hybrid E/M cells, we agree that demonstrating the localization of ABCA1 at the plasma membrane is important, and we have included additional experiments to address this point.

We also examined the expression of the major ACAT isoform in the kidney, SOAT1, across RCC cell lines. However, its expression did not correlate with that of Snail (Figure 4B), suggesting that SOAT1 is constitutively expressed at a certain level regardless of Snail expression. The details of these additional experiments are provided in the point-by-point responses below.

Reviewer #2 (Public review):

Summary:

In this study, the authors discovered that the chemoresistance in RCC cell lines correlates with the expression levels of the drug transporter ABCA1 and the EMT-related transcription factor Snail. They demonstrate that Snail induces ABCA1 expression and chemoresistance, and that ABCA1 inhibitors can counteract this resistance. The study also suggests that Snail disrupts the cholesterol-sphingomyelin (Chol/SM) balance by repressing the expression of enzymes involved in very long-chain fatty acid-sphingomyelin synthesis, leading to excess free cholesterol. This imbalance activates the cholesterol-LXR pathway, inducing ABCA1 expression. Moreover, inhibiting cholesterol esterification suppresses Snail-positive cancer cell growth, providing potential lipid-targeting strategies for invasive cancer therapy.

Strengths:

This research presents a novel mechanism by which the EMT-related transcription factor Snail confers drug resistance by altering the Chol/SM balance, introducing a previously unrecognized role of lipid metabolism in the chemoresistance of cancer cells. The focus on lipid balance, rather than individual lipid levels, is a particularly insightful approach. The potential for targeting cholesterol detoxification pathways in Snail-positive cancer cells is also a significant therapeutic implication.

Weaknesses:

The study's claim that Snail-induced ABCA1 is crucial for chemoresistance relies only on pharmacological inhibition of ABCA1, lacking additional validation. The causal relationship between the disrupted Chol/SM balance and ABCA1 expression or chemoresistance is not directly supported by data. Some data lack quantitative analysis.

We thank the reviewer for his/her insightful and constructive comments. In response, we have performed additional experiments using complementary approaches to further substantiate the contribution of Snail-induced ABCA1 expression to chemoresistance. Furthermore, to clarify the causal relationship between reduced sphingomyelin biosynthesis and ABCA1 expression, we conducted new experiments showing that supplementation with sphingolipids attenuates ABCA1 upregulation (Figure 3H). The details of these additional experiments are described in the point-by-point responses below.

Reviewer #1 (Recommendations for the authors):

In this paper, the authors reveal that snail expression in EMT-cells leads to an imbalance between cholesterol and sphingomyelin via a transcriptional repression of enzymes involved in the biosynthesis of sphingomyelin.

This paper is interesting and highlights how the imbalance of lipids would impact chemotherapy resistance. However, I have a few comments.

In Figure 2 in Eph4 cells, while filipin staining appears exclusively at the plasma membrane in the case of EpH4-snail cells filipin staining is also intracellular. It seems plausible that all filipin-positive intracellular staining is not exclusively in LDs, authors should therefore try to colocalize filipin with other intracellular markers. To this aim, authors might want to use topfluocholesterol-probe for instance.

We examined the distribution of TopFluor-cholesterol in hybrid E/M cells (Figure 2H) and found that TopFluor-cholesterol colocalizes with lipid droplets. In addition, we analyzed the colocalization between intracellular filipin signals and organelle-specific proteins, ADRP (lipid droplets) and LAMP1 (lysosomes) (Figure 2I). Since filipin binds exclusively to unesterified cholesterol, filipin signals did not colocalize with ADRP. Instead, we observed colocalization of filipin with LAMP1, suggesting that cholesterol accumulates in hybrid E/M cells in both esterified and unesterified forms.

In Figure 3, the authors reveal that the exogenous expression of the snail alters the ratio of cholesterol to sphingomyelin. The authors should reveal where is found the intracellular cholesterol and intracellular sphingomyelin within these cells Eph4-snail.

To investigate the lipid composition of the plasma membrane, we utilized lipid-binding protein probes, D4 (for cholesterol) and lysenin (for sphingomyelin) (Figures 2L and 2M). We found that the plasma membrane cholesterol content was not affected by EMT, whereas sphingomyelin levels were markedly decreased. In addition, intracellular cholesterol was visualized (Comment 1-1; Figures 2E–2K). On the other hand, because visualization of intracellular sphingomyelin is technically challenging, we were unable to include this analysis in the present study. We consider this an important direction for future investigation.

Regarding the model described in panel K of Figure 3. I would expect that the changes in lipid-membrane organization depicted in panel K should affect the pattern of GM1 toxin for instance or the motility of raft-associated proteins for instance. The authors could perform these experiments in order to sustain the change of lipid plasma membrane organization.

We attempted staining with FITC–cholera toxin to visualize GM1, but both EpH4 and EpH4–Snail cells exhibited very low levels of GM1, resulting in minimal or no detectable staining (data not shown). Instead, to assess the impact of decreased sphingomyelin on the overall biophysical properties of the plasma membrane, we used a plasma membrane–specific lipid-order probe, FπCM–SO₃ (Figures 2N–2P and Figure 2—figure supplement 3). We found that the plasma membrane of EpH4–Snail cells was more disordered (fluidized), suggesting that the overall properties of the plasma membrane are altered by ectopic expression of Snail.

Another issue is the intracellular localization of ABCA1 in Eph4-Snail cells. Knowing that a change in the cholesterol/sphingomyelin ratio can also modify intracellular protein trafficking, it seems important to analyze the intracellular localization of ABCA1 in EPh4-Snail cells.

We performed immunofluorescence microscopy for ABCA1 and found that ABCA1 was mainly localized at the plasma membrane in EpH4–Snail cells (Figure 1M).

As for the data on ACAT inhibition, we expect an increase in ACAT activity and protein levels in EMT cells overexpressing Snail. The authors should also investigate this point.

As noted in our response to the public review, we examined the expression of the major ACAT isoform in the kidney, SOAT1, across RCC cell lines. However, its expression did not correlate with Snail (Figure 4B), suggesting that SOAT1 is expressed at sufficient levels even in cells with low Snail expression. We agree that measuring ACAT activity would be important, as ACATs are regulated at multiple levels. However, we consider this to be beyond the scope of the present study and plan to address it in future work.

Minor comments

I do not understand why in the text, Figure S1 appears after Figure S2. The authors might want to change the numbering of these two figures.

We thank the reviewer for pointing this out. We have corrected the numbering of the supplementary figures so that Figure S1 now appears before Figure S2 in both the text and the revised figure legends.

Page 5, lane 20 Figure 1I instead of 1H.

Page 6, lane 2, Figure 1J instead of 1I, and lane 9 Figure 1H instead of 1I.

We thank the reviewer for carefully checking the figure references. We have corrected the figure numbering errors in the text as suggested.

Reviewer #2 (Recommendations for the authors):

For Figures 1B, 1H, 1J, 2B, 2C, 3G, S3A, and S3B, to enhance data reliability, it is necessary to conduct a quantitative analysis of the Western blot data. The average values from at least three biological replicates should be calculated, with statistical significance assessed.

We have conducted quantitative analyses of the Western blot data for Figures 1B, 1H, 1J, 2B, 2C, 3G, S3A, and S3B. Band intensities from at least three independent biological replicates were quantified, and the mean values with statistical significance are now presented in the revised figures.

For Figures 1D, 2A, 2D, and S2, the images of cells or tissues should not rely solely on selected fields. Quantitative analysis is required, and the mean values from at least three biological replicates should be provided with statistical significance testing.

We have performed quantitative analyses for Figures 1D, 2A, 2D, and S2. The quantification was based on data from at least three independent biological replicates, and the mean values with statistical significance are now included in the revised figures.

For Figures 1A, 1G, 4, and S5, evaluating ABCA1's involvement in drug resistance based solely on CsA treatment is insufficient. Demonstrating the loss of drug resistance through ABCA1 knockdown or knockout is necessary.

We generated ABCA1 knockout EpH4–Snail cells and examined their resistance to nitidine chloride. However, knockout of ABCA1 alone did not affect resistance to the compound (Figure 2 - figure supplement 2). This may be due to secondary metabolic alterations induced by ABCA1 loss or compensatory upregulation of other LXR-induced cholesterol efflux transporters. Instead, we demonstrated that treatment with the LXR inhibitor GSK2033 reduced the nitidine chloride resistance of EpH4–Snail cells (Figure 2C), supporting the idea that enhanced efflux of antitumor agents through the LXR–ABCA1–mediated cholesterol efflux pathway contributes to nitidine chloride resistance.

For Figure 3, to establish a causal relationship between changes in the Chol/SM balance and ABCA1 expression, it is important to test whether modifying cholesterol and SM levels to disrupt this balance affects ABCA1 expression.

Regarding causality, as shown in Figure 2, we have already demonstrated that reducing cholesterol levels in EpH4–Snail cells decreases ABCA1 expression. To further explore this relationship, we examined whether increasing sphingomyelin levels by adding ceramide to the culture medium—thereby restoring the sphingomyelin-to-cholesterol ratio—would reduce ABCA1 expression (Figure 3H). Indeed, supplementation with C22:0 ceramide decreased ABCA1 expression, suggesting that downregulation of the VLCFA-sphingomyelin biosynthetic pathway triggers ABCA1 upregulation. Collectively, these findings support a causal relationship between the Chol/SM balance and ABCA1 expression.

In Figure 3, if there is any information on differences in cholesterol affinity between LCFA-SM and VLCFA-SM, it would be beneficial to include it in the manuscript.

Differences in cholesterol affinity between LCFA-SM and VLCFA-SM in cellular membranes remain controversial and have yet to be fully elucidated. The decrease in cell surface sphingomyelin content, evaluated by lysenin staining (Figure 2L), was more pronounced than that of total sphingomyelin (Figure 3A). Given that VLCFA-SMs have been suggested to undergo distinct trafficking during recycling from endosomes to the plasma membrane (Koivusalo et al. Mol Biol Cell 2007), their reduction may lead to decreased plasma membrane sphingomyelin content by altering its intracellular distribution. We have added this discussion to the revised manuscript.

In Figure 3F, it is recommended to assess housekeeping gene expression as a control. Quantitative real-time PCR should be performed, and the average values from at least three biological replicates should be presented.

We have performed quantitative RT-PCR analysis. The average values from at least three independent biological replicates are presented in Figure 3G.

For Figure 3F, to show whether the reduction of CERS3 or ELOVL7 affects the Chol/SM balance and ABCA1 expression, it is necessary to investigate the phenotypes following the knockdown or knockout of these enzymes.

We fully agree that phenotypic analyses of epithelial cells lacking CerS3 or ELOVL7 would provide valuable insights. However, we consider such investigations to be beyond the scope of the present study and plan to pursue them in future work.

Clarifying whether similar phenotypes are induced by other EMT-related transcription factors, or if they are specific to Snail, would be beneficial.

We agree that examining whether similar phenotypes are induced by other EMT-related transcription factors would be highly valuable for understanding the broader EMT network. However, as the focus of the present study is on lipid metabolic alterations associated with EMT—particularly the imbalance between sphingomyelin and cholesterol—we consider this investigation to be beyond the scope of the current work and plan to address it in future studies.

There are errors in figure citations within the text that need correction:

p.9 l.18 Fig. 3D → Fig. 3G

p.9 l.22 Fig. 3I → Fig. 3H

p.9 l.23 Fig. S2 → Fig. S4

p.10 l.6 Fig. 3J → Fig. 1J

p.10 l.8 Fig. 3J → Fig. 1J

p.10 l.9 Fig. 3K → Fig. 3I

p.10 l.12 Fig. 3H → Fig. 3J

p.10 l.14 Fig. 2D and Fig. S4 → Fig. 2G and Fig. S4D

We thank the reviewer for carefully pointing out these citation errors. We have corrected all figure references in the text as suggested.

Author response:

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

Reviewer #1 (Public review):

Summary: 

This study builds off prior work that focused on the molecule AA147 and its role as an activator of the ATF6 arm of the unfolded protein response. In prior manuscripts, AA147 was shown to enter the ER, covalently modify a subset of protein disulfide isomerases (PDIs), and improve ER quality control for the disease-associated mutants of AAT and GABAA. Unsuccessful attempts to improve the potency of AA147 have led the authors to characterize a second hit from the screen in this study: the phenylhydrazone compound AA263. The focus of this study on enhancing the biological activity of the AA147 molecule is compelling, and overcomes a hurdle of the prior AA147 drug that proved difficult to modify. The study successfully identifies PDIs as a shared cellular target of AA263 and its analogs. The authors infer, based on the similar target hits previously characterized for AA147, that PDI modification accounts for a mechanism of action for AA263. 

Strengths: 

The authors are able to establish that, like AA147, AA263 covalently targets ER PDIs. The work establishes the ability to modify the AA263 molecule to create analogs with more potency and efficacy for ATF6 activation. The "next generation" analogs are able to enhance the levels of functional AAT and GABAA receptors in cellular models expressing the Z-variant of AAT or an epilepsy-associated variant of the GABAA receptor, outlining the therapeutic potential for this molecule and laying the foundation for future organism-based studies. 

We thank the reviewer for the positive comments on our manuscript. We address the reviewers remaining comments on our work, as described below.

Weaknesses: 

Arguably, the work does not fully support the statement provided in the abstract that the study "reveals a molecular mechanism for the activation of ATF6". The identification of targets of AA263 and its analogs is clear. However, it is a presumption that the overlap in PDIs as targets of both AA263 and AA147 means that AA263 works through the PDIs. While a likely mechanism, this conclusion would be bolstered by establishing that knockdown of the PDIs lessens drug impact with respect to ATF6 activation. 

We thank the reviewer for this comment. We previously showed that genetic depletion of different PDIs modestly impacts ATF6 activation afforded by ATF6 activating compound such as AA147 (see Paxman et al (2018) ELIFE). However, as discussed in this manuscript, the ability for AA147 and AA263 to activate ATF6 signaling is mediated through polypharmacologic targeting of multiple different PDIs involved in regulating the redox state of ATF6. Thus, individual knockdowns are predicted to only minimally impact the ability for AA263 and its analogs to activate ATF6 signaling. 

To address this comment, we have tempered our language regarding the mechanism of AA263-dependent ATF6 activation through PDI targeting described herein to better reflect the fact that we have not explicitly proven that PDI targeting is responsible for this activity, as highlighted below:

“Page 7, Line 158: “Intriguingly, 12 proteins were shared between these two conditions, including 7 different ER-localized PDIs (Fig. 1H). This includes PDIs previously shown to regulate ATF6 activation including TXNDC12/ERP18.[45,46] These results are similar to those observed when comparing proteins modified by the selective ATF6 activating compound AA147^yne and AA132^yne.[38] Further, we found that the extent of labeling for PDIs including PDIA1, PDIA4, PDIA6, and TMX1, but not TXNDC12, showed greater modification by AA132^yne, as compared to AA263^yne (Fig. 1I). Similar results were observed for AA147^yne.[38] This suggests that, like AA147, the selective activation of ATF6 afforded by AA263 is likely attributed to the modifications of a subset of multiple different ER-localized PDIs by this compound.”

Alternatively, it has previously been suggested that the cell-type dependent activity of AA263 may be traced to the presence of cell-type specific P450s that allow for the metabolic activation of AA263 or cell-type specific PDIs (Plate et al 2016; Paxman et al 2018). If the PDI target profile is distinct in different cell types, and these target difference correlates with ATF6-induced activity by AA263, that would also bolster the authors' conclusion. 

As highlighted by the reviewer, different ER oxidases (e.g., P450s) could differentially influence activation of compounds such as AA263 to promote PDI modification and subsequent ATF6 activation. The specific ER oxidases responsible for AA263 activation are currently unknown; however, we anticipate that multiple different enzymes can promote this activity making it difficult to discern the specific contributions of any one oxidase. We have made this point clearer in the revised submission, as below:

Page 7, Line 169: “This specificity for ER proteins instead suggests the localized generation of AA263 quinone methides at the ER membrane, likely through metabolic activation by different ER localized oxidases, which has been previously been shown to contribute to the selective modification of ER proteins afforded by other compounds such as AA147 [49]”   

Reviewer #2 (Public review):

Modulating the UPR by pharmacological targeting of its sensors (or regulators) provides mostly uncharted opportunities in diseases associated with protein misfolding in the secretory pathway. Spearheaded by the Kelly and Wiseman labs, ATF6 modulators were developed in previous years that act on ER PDIs as regulators of ATF6. However, hurdles in their medicinal chemistry have hampered further development. In this study, the authors provide evidence that the small molecule AA263 also targets and covalently modifies ER PDIs, with the effect of activating ATF6. Importantly, AA263 turned out to be amenable to chemical optimization while maintaining its desired activity. Building on this, the authors show that AA263 derivatives can improve the aggregation, trafficking, and function of two disease-associated mutants of secretory pathway proteins. Together, this study provides compelling evidence for AA263 (and its derivatives) being interesting modulators of ER proteostasis. Mechanistic details of its mode of action will need more attention in future studies that can now build on this.

We thank the reviewer for their positive comments on our manuscript. We address the reviewer’s specific queries on our work, as outlined below. 

In detail, the authors provide strong evidence that AA263 covalently binds to ER PDIs, which will inhibit the protein disulfide isomerase activity. ER PDIs regulate ATF6, and thus their finding provides a mechanistic interpretation of AA263 activating the UPR. It should be noted, however, that AA263 shows broad protein labeling (Figure 1G), which may suggest additional targets, beyond the ones defined as MS hits in this study. 

This is true. We do show broad proteome-wide labeling with AA263^yne, which are largely reflected in the hits identified by MS beyond PDI family members. It is possible that other observed engaged targets, in addition to PDIs, may contribute to the activation of ATF6 signaling. Regardless, our MS analysis clearly shows that the compounds modified by AA263 are enriched for PDIs, further supporting our model whereby AA263-dependent PDI modification is likely responsible for ATF6 activation. 

Also, a further direct analysis of the IRE1 and PERK pathways (activated or not by AA263) would have been a benefit, as e.g., PDIA1, a target of AA263, directly regulates IRE1 (Yu et al., EMBOJ, 2020), and other PDIs also act on PERK and IRE1. The authors interpret modest activation of IRE1/PERK target genes (Figure 2C) as an effect on target gene overlap, indeed the most likely explanation based on their selective analyses on IRE1 (ERdj4) and PERK (CHOP) downstream genes, but direct activation due to the targeting of their PDI regulators is also a possible explanation. 

While we do observe mild increases in IRE1/XBP1s target genes, we do not observe significant increases in PERK/ISR target genes in cells treated with optimized AA263 analogs (see Fig. 2C). We previously showed that genetic ATF6 activation leads to a modest increase in IRE1/XBP1s target genes, reflecting the overlap in target genes of the IRE1/XBP1s and ATF6 pathways (see Shoulders et al (2013) Cell Reports). However, with our data, we cannot explicitly rule out the possibility that the mild increase in IRE1/XBP1s target genes reflects direct IRE1/XBP1s activation, as suggested by the reviewer. To address this, we have adapted the text to highlight this point, now specifically referring to preferential ATF6 activation afforded by these compounds, as below:

Page 5, Line 100: “In addition to finding AA147, our original high-throughput screen also identified the phenylhydrazone compound AA263 as a compound that preferentially activates the ATF6 arm of the UPR [26]”  

Further key findings of this paper are the observed improvement of AAT behavior and GABAA trafficking and function. Further strength to the mechanistic conclusion that ATF6 activation causes this could be obtained by using ATF6 inhibitors/knockouts in the presence of AA263 (as the target PDIs may directly modulate the behavior of AAT and/or GABAA). 

AA263 and related compounds could influence ER proteostasis of destabilized proteins through multiple mechanisms including ATF6 activation or direct modification of a subset of PDIs. We previously showed that AA263-dependent enhancement of A1AT-Z secretion and activity can be largely attributed to ATF6 activation (see Sun et al (2023) Cell Chem Biol). In the revised submission, we now show that increased levels of g2(R177G) afforded by treatment with AA263^yne are partially blocked by co-treatment with the ATF6 inhibitor Ceapin-A7 (CP7), highlighting the contributions of ATF6 activation for this phenotype (Fig. S5B,C). Intriguingly, this result also demonstrates the benefit for targeting ER proteostasis using compounds such as our optimized AA263 analogs, as this approach allows us to enhance ER proteostasis of destabilized proteins through multiple mechanisms. We further expand on this specific point in the revised manuscript as below:

Page 14, Line 375: “AA263 and its related analogs can influence ER proteostasis in these models through different mechanisms including ATF6-dependent remodeling of ER proteostasis and direct alterations to the activity of specific PDIs.(*) Consistent with this, we show that pharmacologic inhibition of ATF6 only partially blocks increases of g2(R177G) afforded by treatment with AA263^yne, highlighting the benefit for targeting multiple aspects of ER proteostasis to enhance ER proteostasis of this diseaserelevant GABA_A variant. While additional studies are required to further deconvolute the relative contributions of these two mechanisms on the protection afforded by our optimized compounds, our results demonstrate the potential for these compounds to enhance ER proteostasis in the context of different protein misfolding diseases.”  

Along the same line, it also warrants further investigation why the different compounds, even if all were used at concentrations above their EC50, had different rescuing capacities on the clients.

This is an interesting question that we are continuing to study. While in general, we observe fairly good correlation between ATF6 activation and correction of diseases of ER proteostasis linked to proteins such as A1AT-Z or GABA_A receptors, as the reviewer points out, we do find some compounds are more efficient at correcting proteostasis than others activate ATF6 to similar levels. We attribute this to differences in either labeling efficiency of PDIs or differential regulation of various ER proteostasis factors, although that remains to be further defined. As we continue working with these (and other) compounds, we will focus on defining a more molecular basis for these findings. 

Together, the study now provides a strong basis for such in-depth mechanistic analyses.

We agree and we are continuing to pursue the mechanistic basis of ER proteostasis remodeling afforded by these and related compounds. 

Reviewer #3 (Public review):

Summary: 

This study aims to develop and characterize phenylhydrazone-based small molecules that selectively activate the ATF6 arm of the unfolded protein response by covalently modifying a subset of ER-resident PDIs. The authors identify AA263 as a lead scaffold and optimize its structure to generate analogs with improved potency and ATF6 selectivity, notably AA263-20. These compounds are shown to restore proteostasis and functional expression of disease-associated misfolded proteins in cellular models involving both secretory (AAT-Z) and membrane (GABAA receptor) proteins. The findings provide valuable chemical tools for modulating ER proteostasis and may serve as promising leads for therapeutic development targeting protein misfolding diseases.

Strengths: 

(1) The study presents a well-defined chemical biology framework integrating proteomics, transcriptomics, and disease-relevant functional assays. 

(2) Identification and optimization of a new electrophilic scaffold (AA263) that selectively activates ATF6 represents a valuable advance in UPR-targeted pharmacology.

(3) SAR studies are comprehensive and logically drive the development of more potent and selective analogs such as AA263-20.

(4) Functional rescue is demonstrated in two mechanistically distinct disease models of protein misfolding-one involving a secretory protein and the other a membrane protein-underscoring the translational relevance of the approach. 

We thank the reviewer for their positive comments related to our work. We address specific weaknesses highlighted by the reviewer, as outlined below. 

Weaknesses: 

(1) ATF6 activation is primarily inferred from reporter assays and transcriptional profiling; however, direct evidence of ATF6 cleavage is lacking.

While ATF6 trafficking and processing can be visualized in cell culture models following severe ER insults (e.g., Tg, Tm), we showed previously that the more modest activation afforded by pharmacologic activators such as AA147 and AA263 cannot be easily visualized by monitoring ATF6 processing (see Plate et al (2016) ELIFE). As we have shown in numerous other manuscripts, we have established a transcriptional profiling approach that accurately defines ATF6 activation. We use that approach to confirm preferential ATF6 activation in this manuscript. We feel that this is sufficient for confirming ATF6 activation. However, we also now include data showing that co-treatment with ATF6 inhibitors (e.g., CP7) blocks increased expression of ATF6 target genes induced by our prioritized compound AA263^yne (Fig. S1B). This further supports our assertion that this compound activates ATF6 signaling.  

(2) While the mechanism involving PDI modification and ATF6 activation is plausible, it remains incompletely characterized. 

We thank the reviewer for this comment. We previously showed that genetic depletion of different PDIs modestly impacts ATF6 activation afforded by ATF6 activating compound such as AA147. However, as discussed in this manuscript, the ability for AA147 and AA263 to activate ATF6 signaling is mediated through polypharmacologic targeting of multiple different PDIs involved in regulating ATF6 redox. Thus, individual knockdowns are predicted to only minimally impact the ability for AA263 and its analogs to activate ATF6 signaling. 

To address this comment, we have tempered out language regarding the mechanism of AA263-dependent ATF6 activation through PDI targeting described herein to better reflect the fact that we have not explicitly proven that PDI targeting is responsible for this activity, as highlighted below:

Page 7, Line 158: “Intriguingly, 12 proteins were shared between these two conditions, including 7 different ER-localized PDIs (Fig. 1H). This includes PDIs previously shown to regulate ATF6 activation including TXNDC12/ERP18.[45,46] These results are similar to those observed when comparing proteins modified by the selective ATF6 activating compound AA147^yne and AA132^yne.[38] Further, we found that the extent of labeling for PDIs including PDIA1, PDIA4, PDIA6, and TMX1, but not TXNDC12, showed greater modification by AA132^yne, as compared to AA263^yne (Fig. 1I). Similar results were observed for AA147^yne[38] This suggests that, like AA147, the selective activation of ATF6 afforded by AA263 is likely attributed to the modifications of a subset of multiple different ER-localized PDIs by this compound.”

(3) No in vivo data are provided, leaving the pharmacological feasibility and bioavailability of these compounds in physiological systems unaddressed.

We are continuing to test the in vivo activity of these compounds in work outside the scope of this initial study. 

Reviewer #1 (Recommendations for the authors): 

(1) First page of the discussion, last sentence. "We previously showed the relatively labeling of PDI modification directly impacts..." should be reworded.

Thank you. We have corrected this in the revised manuscript. 

(2) What is the rationale for measuring ERSE-Fluc activity at 18 h but RNAseq at 6 h? What is known about the timing of action for AA263?

Compound-dependent activation of luciferase reporters requires the translation and accumulation of the luciferase protein for sufficient signal, while qPCR does not. We normally use longer incubations for reporter assays to ensure that we have sufficient quantity of reporter protein to accurately monitor activation. We have found that AA263 can rapidly increase ATF6 activity, with gene expression increases being observed after only a few hours of treatment. This is consistent with the proposed mechanism of ATF6 activation discussed herein involving metabolic activation and subsequent PDI modification.   

(3) Figure 1 panel E and Figure S2 panel B. Are these the same data for AA263 and AA263yne, with the AA2635 added to the plot for Figure S2? If so, it would be nice to note that panel B represents data from 3 of the replicates that are shown in Figure 1 (n=6).

Yes. The AA263 and AA263^yne data shown in Fig. 1E and Fig. S2B are the same data, as these experiments were performed at the same time. We apologize for this oversight, which has now been corrected in the revised version. Note that there were n=3 replicates for the dose response shown in Fig. 1E, which we corrected in the figure legend as below:

Fig. S2B Figure Legend: “B. Activation of the ERSE-FLuc ATF6 reporter in HEK293T cells treated for 18 h with the indicated concentration of AA263, AA263^yne, or AA263-5. Error bars show SEM for n= 3 replicates. The data for AA263 and AA263^yne is the same as that shown in Fig. 1E and are shown for comparison.” 

(4) Figure S3. The legend notes 5 µM AA263-yne and 20 µM analog, whereas the figure itself outlines the same ratio but different concentrations: 10 µM and 40 µM.

We apologize for this mistake in the legend, which has been corrected. The information in the figure is correct. 

Reviewer #2 (Recommendations for the authors): 

(1) The activation mechanism of ATF6 is still debated (really trafficking as a monomer?); the authors may want to word more carefully here. 

We agree. We have corrected this in the revised manuscript to indicate that increased populations of reduced ATF6 traffic for proteolytic processing. 

(2) In Figure 1B, below the figure, mM is written for BME, but micromolar is meant.

Thank you. This has been corrected in the revised manuscript. 

(3) The authors may want to make clearer, why BME does not completely inhibit AA263 and does not cause ER stress itself under the conditions tested.

The addition of BME in our experiments is designed to shift the redox potential of the cell to increase intracellular thiol reagents, such as glutathione, that can quench ‘activated’ AA263 and its analogs. However, BME is actively being oxidized upon addition and the intracellular redox environment can rapidly equilibrate following BME addition. Thus, we do not expect that AA263 or other metabolically activated compounds will be fully quenched using this approach, as is observed. This is consistent with other experiments where we show that the use of these types of reducing agents do not fully suppress the activity of reactive molecules, instead shifting their dosedependent activation of specific pathways.  

(4) The data in Figure 4C seems to disagree with the other data on the tested compounds; this should be clarified. 

It is unclear to what the reviewer is referring. The data in 4C shows that treatment with our optimized AA263 analogs improved elastase inhibition afforded by secreted A1AT, as would be predicted. 

(5) PDIs that have been shown to regulate ATF6 should be discussed in more detail in the light of the presented data/interactome (e.g., ERp18).

Thank you for the suggestion. We now explicitly note that AA263^yne covalent modifies TXNDC12/ERP18 in our proteomic dataset. However, we also note that there is no difference in labeling of this specific PDI between AA263^yne and AA132^yne. This may indicate that the targeting of this protein is responsible for the larger levels of ATF6 activation afforded by both these compounds relative to AA147, with the activation of other UPR pathways afforded by AA132 resulting from increased labeling of other PDIs. We are now exploring this possibility in work outside the scope of this current manuscript. 

Page 7 Line 158: “Intriguingly, 12 proteins were shared between these two conditions, including 7 different ER-localized PDIs (Fig. 1H). This includes PDIs previously shown to regulate ATF6 activation including TXNDC12/ERP18.[45,46] These results are similar to those observed when comparing proteins modified by the selective ATF6 activating compound AA147^yne and AA132^yne.[38] Further, we found that the extent of labeling for PDIs including PDIA1, PDIA4, PDIA6, and TMX1, but not TXNDC12, showed greater modification by AA132^yne, as compared to AA263^yne (Fig. 1I). Similar results were observed for AA147^yne [38] This suggests that, like AA147, the selective activation of ATF6 afforded by AA263 is likely attributed to the modifications of a subset of multiple different ER-localized PDIs by this compound.”

Reviewer #3 (Recommendations for the authors):

(1) Please consider adding detection of ATF6 cleavage by Western blot as direct evidence of AA263-induced ATF6 activation, to substantiate the central mechanistic claim.

While ATF6 trafficking and processing can be visualized in cell culture models following severe ER insults (e.g., Tg, Tm), we showed previously that the more modest activation afforded by pharmacologic activators such as AA147 and AA263 cannot be easily visualized through monitoring ATF6 proteolytic processing by western blotting (see Plate et al (2016) ELIFE). As we have shown in numerous other manuscripts, we have established a transcriptional profiling approach that accurately defines ATF6 activation. We use that approach to confirm preferential ATF6 activation in this manuscript. We feel that this is sufficient for confirming ATF6 activation. However, we also now include qPCR data showing that co-treatment with ATF6 inhibitors (e.g., CP7) blocks increased expression of ATF6 target genes induced by our prioritized compounds. 

(2) To strengthen causal inference, loss-of-function experiments such as PDI knockdown, cysteine mutant inactivation, or reconstitution studies may be informative.

We thank the reviewer for this comment. We previously showed that genetic depletion of different PDIs modestly impacts ATF6 activation afforded by ATF6 activating compound such as AA147. However, as discussed in this manuscript, the ability for AA147 and AA263 to activate ATF6 signaling is mediated through polypharmacologic targeting of multiple different PDIs involved in regulating ATF6 redox state rather than a single PDI family member. Thus, individual knockdowns are predicted to only minimally impact the ability for AA263 and its analogs to activate ATF6 signaling. 

To address this comment, we have tempered out language regarding the mechanism of AA263-dependent ATF6 activation through PDI targeting described herein to better reflect the fact that we have not explicitly proven that PDI targeting is responsible for this activity.

(3) Since β-mercaptoethanol inhibits ATF6 activation, it would be helpful to examine whether DTT also suppresses the activity of AA263 or its analogs, to clarify the redox sensitivity of the mechanism.

The use of reducing agents stronger than BME, such as DTT, globally activates the UPR, including the ATF6 arm of the UPR. Thus, we are unable to perform the requested experiments. We specifically use BME because it is a sufficiently mild reducing agent that can quench reactive metabolites (e.g., activated AA263 analogs) through alterations in cellular glutathione levels without globally activating the UPR.  

(4) Given the electrophilic nature of AA263, which may allow it to react with endogenous thiols (e.g., glutathione or cysteine), a brief discussion or experimental validation of this potential liability would enhance the interpretation of in vivo applicability.

Metabolically activated AA263, like AA147, can be quenched by endogenous thiols such as glutathione. However, treatment with our metabolically activatable electrophiles AA147 and AA263 , either in vitro or in vivo, does not seem to induce activation of the NRF2-regulated oxidative stress response (OSR) in the cell lines used in this manuscript (e.g., Fig. S2C). This suggests that treatment with these compounds does not globally disrupt the intracellular redox state, at least in the tested cell lines. While AA147 has been shown to activate NRF2 in specifical neuronal cell lines and in primary neurons, AA147 does not activate NRF2 signaling in other nonneuronal cell lines or other tissues (see Rosarda et al (2021) ACS Chem Bio). We are currently testing the potential for AA263 to similarly activate adaptive NRF2 signaling in neuronal cells. Regardless, AA147, which functions through a similar mechanism to that proposed for AA263, has been shown to be beneficial in multiple models of disease both in vitro and in vivo. This indicates that this mechanism of action is suitable for continued translational development to mitigate pathologic ER proteostasis disruption observed in diverse types of human disease.  

(5) Evaluation of in vivo activity, such as BiP induction in the liver following intraperitoneal administration of AA263-20 or related analogs, could substantially increase the translational impact of the work.

We are continuing to probe the activity of our optimized AA263 analogs in vivo in work outside the scope of this current manuscript. We thank the reviewer for this suggestion. 

(6) The degree of BiP induction may also be contextualized by comparison with known ER stress inducers such as thapsigargin or tunicamycin, ideally by providing relative dose-equivalent responses.

We are not sure to what the reviewer is referring. We show comparative activation of ATF6 in cells treated with the ER stressor Tg and our compounds by both reporter assay (e.g., Fig. 2B) and qPCR of the ATF6 target gene BiP (HSPA5) (Fig. S2A). We feel that this provides context for the more physiologic levels of ATF6 activation afforded by these compounds.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

This paper presents a computational model of the evolution of two different kinds of helping ("work," presumably denoting provisioning, and defense tasks) in a model inspired by cooperatively breeding vertebrates. The helpers in this model are a mix of previous offspring of the breeder and floaters that might have joined the group, and can either transition between the tasks as they age or not. The two types of help have differential costs: "work" reduces "dominance value," (DV), a measure of competitiveness for breeding spots, which otherwise goes up linearly with age, but defense reduces survival probability. Both eventually might preclude the helper from becoming a breeder and reproducing. How much the helpers help, and which tasks (and whether they transition or not), as well as their propensity to disperse, are all evolving quantities. The authors consider three main scenarios: one where relatedness emerges from the model, but there is no benefit to living in groups, one where there is no relatedness, but living in larger groups gives a survival benefit (group augmentation, GA), and one where both effects operate. The main claim is that evolving defensive help or division of labor requires the group augmentation; it doesn't evolve through kin selection alone in the authors' simulations.

This is an interesting model, and there is much to like about the complexity that is built in. Individual-based simulations like this can be a valuable tool to explore the complex interaction of life history and social traits. Yet, models like this also have to take care of both being very clear on their construction and exploring how some of the ancillary but potentially consequential assumptions affect the results, including robust exploration of the parameter space. I think the current manuscript falls short in these areas, and therefore, I am not yet convinced of the results. In this round, the authors provided some clarity, but some questions still remain, and I remain unconvinced by a main assumption that was not addressed.

Based on the authors' response, if I understand the life history correctly, dispersers either immediately join another group (with 1-the probability of dispersing), or remain floaters until they successfully compete for a breeder spot or die? Is that correct? I honestly cannot decide because this seems implicit in the first response but the response to my second point raises the possibility of not working while floating but can work if they later join a group as a subordinate. If it is the case that floaters can have multiple opportunities to join groups as subordinates (not as breeders; I assume that this is the case for breeding competition), this should be stated, and more details about how. So there is still some clarification to be done, and more to the point, the clarification that happened only happened in the response. The authors should add these details to the main text. Currently, the main text only says vaguely that joining a group after dispersing " is also controlled by the same genetic dispersal predisposition" without saying how.

In each breeding cycle, individuals have the opportunity to become a breeder, a helper, or a floater. Social role is really just a state, and that state can change in each breeding cycle (see Figure 1). Therefore, floaters may join a group as subordinates at any point in time depending on their dispersal propensity, and subordinates may also disperse from their natal group any given time. In the “Dominance-dependent dispersal propensities” section in the SI, this dispersal or philopatric tendency varies with dominance rank.

We have added: “In each breeding cycle” (L415) to clarify this further.

In response to my query about the reasonableness of the assumption that floaters are in better condition (in the KS treatment) because they don't do any work, the authors have done some additional modeling but I fail to see how that addresses my point. The additional simulations do not touch the feature I was commenting on, and arguably make it stronger (since assuming a positive beta_r -which btw is listed as 0 in Table 1- would make floaters on average be even more stronger than subordinates). It also again confuses me with regard to the previous point, since it implies that now dispersal is also potentially a lifetime event. Is that true?

We are not quite sure where the reviewer gets this idea because we have never assumed a competitive advantage of floaters versus helpers. As stated in the previous revision, floaters can potentially outcompete subordinates of the same age if they attempt to breed without first queuing as a subordinate (step 5 in Figure 1) if subordinates are engaged in work tasks. However, floaters also have higher mortality rates than group members, which makes them have lower age averages. In addition, helpers have the advantage of always competing for an open breeding position in the group, while floaters do not have this preferential access (in Figure S2 we reduce even further the likelihood of a floater to try to compete for a breeding position).

Moreover, in the previous revision (section: “Dominance-dependent dispersal propensities” in the SI) we specifically addressed this concern by adding the possibility that individuals, either floaters or subordinate group members, react to their rank or dominance value to decide whether to disperse (if subordinate) or join a group (if floater). Hence, individuals may choose to disperse when low ranked and then remain on the territory they dispersed to as helpers, OR they may remain as helpers in their natal territory as low ranked individuals and then disperse later when they attain a higher dominance value. The new implementation, therefore, allows individuals to choose when to become floaters or helpers depending on their dominance value. This change to the model affects the relative competitiveness between floaters and helpers, which avoids the assumption that either low- or high-quality individuals are the dispersing phenotype and, instead, allows rank-based dispersal as an emergent trait. As shown in Figure S5, this change had no qualitative impact on the results.

To make this all clearer, we have now added to all of the relevant SI tables a new row with the relative rank of helpers vs floaters. As shown, floaters do not consistently outrank helpers. Rather, which role is most dominant depends on the environment and fitness trade-offs that shape their dispersing and helping decisions.

Some further clarifications: beta_r is a gene that may evolve either positive or negative values, 0 (no reaction norm of dispersal to dominance rank) is the initial value in the simulations before evolution takes place. Therefore, this value may evolve to positive or negative values depending on evolutionary trade-offs. Also, and as clarified in the previous comment, the decision to disperse or not occurs at each breeding cycle, so becoming a floater, for example, is not a lifetime event unless they evolve a fixed strategy (dispersal = 0 or 1). 

Meanwhile, the simplest and most convincing robustness check, which I had suggested last round, is not done: simply reduce the increase in the R of the floater by age relative to subordinates. I suspect this will actually change the results. It seems fairly transparent to me that an average floater in the KS scenario will have R about 15-20% higher than the subordinates (given no defense evolves, y_h=0.1 and H_work evolves to be around 5, and the average lifespan for both floaters and subordinates are in the range of 3.7-2.5 roughly, depending on m). That could be a substantial advantage in competition for breeding spots, depending on how that scramble competition actually works. I asked about this function in the last round (how non-linear is it?) but the authors seem to have neglected to answer.

As we mentioned in the previous comment above, we have now added the relative rank between helpers and floaters to all the relevant SI tables, to provide a better idea of the relative competitiveness of residents versus dispersers for each parameter combination. As seen in Table S1, the competitive advantage of floaters is only marginally in the favor for floaters in the “Only kin selection” implementation. This advantage only becomes more pronounced when individuals can choose whether to disperse or remain philopatric depending on their rank. In this case, the difference in rank between helpers and floaters is driven by the high levels of dispersal, with only a few newborns (low rank) remaining briefly in the natal territory (Table S6). Instead, the high dispersal rates observed under the “Only kin selection” scenario appear to result from the low incentives to remain in the group when direct fitness benefits are absent, unless indirect fitness benefits are substantially increased. This effect is reinforced by the need for task partitioning to occur in an all-or-nothing manner (see the new implementation added to the “Kin selection and the evolution of division of labor” in the Supplementary materials; more details in following comments).

In addition, we specifically chose not to impose this constraint of forcing floaters to be lower rank than helpers because doing so would require strong assumptions on how the floaters rank is determined. These assumptions are unlikely to be universally valid across natural populations (and probably not commonly met in most species) and could vary considerably among species. Therefore, it would add complexity to the model while reducing generalizability.

As stated in the previous revision, no scramble competition takes place, this was an implementation not included in the final version of the manuscript in which age did not have an influence in dominance. Results were equivalent and we decided to remove it for simplicity prior to the original submission, as the model is already very complex in the current stage; we simply forgot to remove it from Table 1, something we explained in the previous round of revisions.

More generally, I find that the assumption (and it is an assumption) floaters are better off than subordinates in a territory to be still questionable. There is no attempt to justify this with any data, and any data I can find points the other way (though typically they compare breeders and floaters, e.g.: https://bioone.org/journals/ardeola/volume-63/issue-1/arla.63.1.2016.rp3/The-Unknown-Life-of-Floaters--The-Hidden-Face-of/10.13157/arla.63.1.2016.rp3.full concludes "the current preliminary consensus is that floaters are 'making the best of a bad job'."). I think if the authors really want to assume that floaters have higher dominance than subordinates, they should justify it. This is driving at least one and possibly most of the key results, since it affects the reproductive value of subordinates (and therefore the costs of helping).

We explicitly addressed this in the previous revision in a long response about resource holding potential (RHP). Once again, we do NOT assume that dispersers are at a competitive advantage to anyone else. Floaters lack access to a territory unless they either disperse into an established group or colonize an unoccupied territory. Therefore, floaters endure higher mortalities due to the lack of access to territories and group living benefits in the model, and are not always able to try to compete for a breeding position.

The literature reports mixed evidence regarding the quality of dispersing individuals, with some studies identifying them as low-quality and others as high-quality, attributing this to them experiencing fewer constraints when dispersing that their counterparts (e.g. Stiver et al. 2007 Molecular Ecology; Torrents‐Ticó, et al. 2018 Journal of Zoology). Additionally, dispersal can provide end-of-queue individuals in their natal group an opportunity to join a queue elsewhere that offers better prospects, outcompeting current group members (Nelson‐Flower et al. 2018 Journal of Animal Ecology). Moreover, in our model floaters do not consistently have lower dominance values or ranks than helpers, and dominance value is often only marginally different.

In short, we previously addressed the concern regarding the relative competitiveness of floaters compared to subordinate group members. To further clarify this point here, we have now included additional data on relative rank in all of the relevant SI tables. We hope that these additions will help alleviate any remaining concerns on this matter.

Regarding division of labor, I think I was not clear so will try again. The authors assume that the group reproduction is 1+H_total/(1+H_total), where H_total is the sum of all the defense and work help, but with the proviso that if one of the totals is higher than "H_max", the average of the two totals (plus k_m, but that's set to a low value, so we can ignore it), it is replaced by that. That means, for example, if total "work" help is 10 and "defense" help is 0, total help is given by 5 (well, 5.1 but will ignore k_m). That's what I meant by "marginal benefit of help is only reduced by a half" last round, since in this scenario, adding 1 to work help would make total help go to 5.5 vs. adding 1 to defense help which would make it go to 6. That is a pretty weak form of modeling "both types of tasks are necessary to successfully produce offspring" as the newly added passage says (which I agree with), since if you were getting no defense by a lot of food, adding more food should plausibly have no effect on your production whatsoever (not just half of adding a little defense). This probably explains why often the "division of labor" condition isn't that different than the no DoL condition.

The model incorporates division of labor as the optimal strategy for maximizing breeder productivity, while penalizing helping efforts that are limited to either work or defense alone. Because the model does not intend to force the evolution of help as an obligatory trait (breeders may still reproduce in the absence of help; k₀ ≠ 0), we assume that the performance of both types of task by the helpers is a non-obligatory trait that complements parental care.

That said, we recognize the reviewer’s concern that the selective forces modeled for division of labor might not be sufficient in the current simulations. To address this, we have now introduced a new implementation, as discussed in the “Kin selection and the evolution of division of labor” section in the SI. In this implementation, division of labor becomes obligatory for breeders to gain a productivity boost from the help of subordinate group members. The new implementation tests whether division of labor can arise solely from kin selection benefits. Under these premises, philopatry and division of labor do emerge through kin selection, but only when there is a tenfold increase in productivity per unit of help compared to the default implementation. Thus, even if such increases are biologically plausible, they are more likely to reflect the magnitudes characteristic of eusocial insects rather than of cooperatively breeding vertebrates (the primary focus of this model). Such extreme requirements for productivity gains and need for coordination further suggest that group augmentation, and not kin selection, is probably the primary driving force particularly in harsh environments. This is now discussed in L210-213.

Reviewer #2 (Public review):

Summary:

This paper formulates an individual-based model to understand the evolution of division of labor in vertebrates. The model considers a population subdivided in groups, each group has a single asexually-reproducing breeder, other group members (subordinates) can perform two types of tasks called "work" or "defense", individuals have different ages, individuals can disperse between groups, each individual has a dominance rank that increases with age, and upon death of the breeder a new breeder is chosen among group members depending on their dominance. "Workers" pay a reproduction cost by having their dominance decreased, and "defenders" pay a survival cost. Every group member receives a survival benefit with increasing group size. There are 6 genetic traits, each controlled by a single locus, that control propensities to help and disperse, and how task choice and dispersal relate to dominance. To study the effect of group augmentation without kin selection, the authors cross-foster individuals to eliminate relatedness. The paper allows for the evolution of the 6 genetic traits under some different parameter values to study the conditions under which division of labour evolves, defined as the occurrence of different subordinates performing "work" and "defense" tasks. The authors envision the model as one of vertebrate division of labor.

The main conclusion of the paper is that group augmentation is the primary factor causing the evolution of vertebrate division of labor, rather than kin selection. This conclusion is drawn because, for the parameter values considered, when the benefit of group augmentation is set to zero, no division of labor evolves and all subordinates perform "work" tasks but no "defense" tasks.

Strengths:

The model incorporates various biologically realistic details, including the possibility to evolve age polytheism where individuals switch from "work" to "defence" tasks as they age or vice versa, as well as the possibility of comparing the action of group augmentation alone with that of kin selection alone.

Weaknesses:

The model and its analysis is limited, which makes the results insufficient to reach the main conclusion that group augmentation and not kin selection is the primary cause of the evolution of vertebrate division of labor. There are several reasons.

First, the model strongly restricts the possibility that kin selection is relevant. The two tasks considered essentially differ only by whether they are costly for reproduction or survival. "Work" tasks are those costly for reproduction and "defense" tasks are those costly for survival. The two tasks provide the same benefits for reproduction (eqs. 4, 5) and survival (through group augmentation, eq. 3.1). So, whether one, the other, or both tasks evolve presumably only depends on which task is less costly, not really on which benefits it provides. As the two tasks give the same benefits, there is no possibility that the two tasks act synergistically, where performing one task increases a benefit (e.g., increasing someone's survival) that is going to be compounded by someone else performing the other task (e.g., increasing that someone's reproduction). So, there is very little scope for kin selection to cause the evolution of labour in this model. Note synergy between tasks is not something unusual in division of labour models, but is in fact a basic element in them, so excluding it from the start in the model and then making general claims about division of labour is unwarranted. I made this same point in my first review, although phrased differently, but it was left unaddressed.

The scope of this paper was to study division of labor in cooperatively breeding species with fertile workers, in which help is exclusively directed towards breeders to enhance offspring production (i.e., alloparental care), as we stated in the previous review. Therefore, in this context, helpers may only obtain fitness benefits directly or indirectly by increasing the productivity of the breeders. This benefit is maximized when division of labor occurs between group members as there is a higher return for the least amount of effort per capita. Our focus is in line with previous work in most other social animals, including eusocial insects and humans, which emphasizes how division of labor maximizes group productivity. This is not to suggest that the model does not favor synergy, as engaging in two distinct tasks enhances the breeders' productivity more than if group members were to perform only one type of alloparental care task. We have expanded on the need for division of labor by making the performance of each type of task a requirement to boost the breeders productivity, see more details in a following comment.

Second, the parameter space is very little explored. This is generally an issue when trying to make general claims from an individual-based model where only a very narrow parameter region has been explored of a necessarily particular model. However, in this paper, the issue is more evident. As in this model the two tasks ultimately only differ by their costs, the parameter values specifying their costs should be varied to determine their effects. Instead, the model sets a very low survival cost for work (yh=0.1) and a very high survival cost for defense (xh=3), the latter of which can be compensated by the benefit of group augmentation (xn=3). Some very limited variation of xh and xn is explored, always for very high values, effectively making defense unevolvable except if there is group augmentation. Hence, as I stated in my previous review, a more extensive parameter exploration addressing this should be included, but this has not been done. Consequently, the main conclusion that "division of labor" needs group augmentation is essentially enforced by the limited parameter exploration, in addition to the first reason above.

We systematically explored the parameter landscape and report in the body of the paper only those ranges that lead to changes in the reaction norms of interest (other ranges are explored in the SI). When looking into the relative magnitude of cost of work and defense tasks, it is important to note that cost values are not directly comparable because they affect different traits. However, the ranges of values capture changes in the reaction norms that lead to rank-depending task specialization.

To illustrate this more clearly, we have added a new section in the SI (Variation in the cost of work tasks instead of defense tasks section) showing variation in y_h, which highlights how individuals trade off the relative costs of different tasks. As shown, the results remain consistent with everything we showed previously: a higher cost of work (high y_h) shifts investment toward defense tasks, while a higher cost of defense (high x_h) shifts investment toward work tasks.

Importantly, additional parameter values were already included in the SI of the previous revision, specifically to favor the evolution of division of labor under only kin selection. Basically, division of labor under only kin selection does happen, but only under conditions that are very restrictive, as discussed in the “Kin selection and the evolution of division of labor” section in the SI. We have tried to make this point clearer now (see comments to previous reviewer above, and to this reviewer right below).

Third, what is called "division of labor" here is an overinterpretation. When the two tasks evolve, what exists in the model is some individuals that do reproduction-costly tasks (so-called "work") and survival-costly tasks (so-called "defense"). However, there are really no two tasks that are being completed, in the sense that completing both tasks (e.g., work and defense) is not necessary to achieve a goal (e.g., reproduction). In this model there is only one task (reproduction, equation 4,5) to which both "tasks" contribute equally and so one task doesn't need to be completed if the other task compensates for it. So, this model does not actually consider division of labor.

Although it is true that we did not make the evolution of help obligatory and, therefore, did not impose division of labor by definition, the assumptions of the model nonetheless create conditions that favor the emergence of division of labor. This is evident when comparing the equilibria between scenarios where division of labor was favored versus not favored (Figure 2 triangles vs circles).

That said, we acknowledge the reviewer’s concern that the selective forces modeled in our simulations may not, on their own, be sufficient to drive the evolution of division of labor under only kin selection. Therefore, we have now added a section where we restrict the evolution of help to instances in which division of labor is necessary to have an impact on the dominant breeder productivity. Under this scenario, we do find division of labor (as well as philopatry) evolving under only kin selection. However, this behavior only evolves when help highly increases the breeders’ productivity (by a factor of 10 what is needed for the evolution of division of labor under group augmentation). Therefore, group augmentation still appears to be the primary driver of division of labor, while kin selection facilitates it and may, under certain restrictive circumstances, also promote division of labor independently (discussed in L210-213).

Reviewer #1 (Recommendations for the authors):

I really think you should do the simulations where floaters do not come out ahead by floating. That will likely change the result, but if it doesn't, you will have a more robust finding. If it does, then you will have understood the problem better.

As we outlined in the previous round of revisions, implementing this change would be challenging without substantially increasing model complexity and reducing its general applicability, as it would require strong assumptions that could heavily influence dispersal decisions. For instance, by how much should helpers outcompete floaters? Would a floater be less competitive than a helper regardless of age, or only if age is equal? If competitiveness depends on equal age, what is the impact of performing work tasks given that workers always outcompete immigrants? Conversely, if floaters are less competitive regardless of age, is it realistic that a young individual would outcompete all immigrants? If a disperser finds a group immediately after dispersal versus floating for a while, is the dominance value reduced less (as would happen to individuals doing prospections before dispersal)? 

Clearly it is not as simple as the referee suggests because there are many scenarios that would need to be considered and many assumptions made in doing this. As we explained to the points above, we think our treatment of floaters is consistent with the definition of floaters in the literature, and our model takes a general approach without making too many assumptions.

Reviewer #2 (Recommendations for the authors):

The paper's presentation is still unclear. A few instances include the following. It is unclear what is plotted in the vertical axes of Figure 2, which is T but T is a function of age t, so this T is presumably being plotted at a specific t but which one it is not said.

The values graphed are the averages of the phenotypically expressed tasks, not the reaction norms per se. We have now rewritten the the axis to “Expressed task allocation T (0 = work, 1 = defense)” to increase clarity across the manuscript.

The section titled "The need for division of labor" in the methods is still very unclear.

We have rephased this whole section to improve clarity.

Author response:

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

Reviewer #1 (Public review):

Nielsen et al have identified a new disease mechanism underlying hypoplastic left heart syndrome due to variants in ribosomal protein genes that lead to impaired cardiomyocyte proliferation. This detailed study starts with an elegant screen in stemcell-derived cardiomyocytes and whole genome sequencing of human patients and extends to careful functional analysis of RP gene variants in fly and fish models. Striking phenotypic rescue is seen by modulating known regulators of proliferation, including the p53 and Hippo pathways. Additional experiments suggest that the cell type specificity of the variants in these ubiquitously expressed genes may result from genetic interactions with cardiac transcription factors. This work positions RPs as important regulators of cardiomyocyte proliferation and differentiation involved in the etiology of HLHS, although the downstream mechanisms are unclear.

We thank Reviewer 1 for the thoughtful assessment of our manuscript. Our point-bypoint responses to the recommendations are provided (Reviewer 1, “Recommendations for the authors”).

Reviewer #2 (Public review):

Tanja Nielsen et al. present a novel strategy for the identification of candidate genes in Congenital Heart Disease (CHD). Their methodology, which is based on comprehensive experiments across cell models, Drosophila and zebrafish models, represents an innovative, refreshing and very useful set of tools for the identification of disease genes, in a field which are struggling with exactly this problem. The authors have applied their methodology to investigate the pathomechanisms of Hypoplastic Left Heart Syndrome (HLHS) - a severe and rare subphenotype in the large spectrum of CHD malformations. Their data convincingly implicates ribosomal proteins (RPs) in growth and proliferation defects of cardiomyocytes, a mechanism which is suspected to be associated with HLHS.

By whole genome sequencing analysis of a small cohort of trios (25 HLHS patients and their parents), the authors investigated a possible association between RP encoding genes and HLHS. Although the possible association between defective RPs and HLHS needs to be verified, the results suggest a novel disease mechanism in HLHS, which is a potentially substantial advance in our understanding of HLHS and CHD. The conclusions of the paper are based on solid experimental evidence from appropriate high- to medium-throughput models, while additional genetic results from an independent patient cohort are needed to verify an association between RP encoding genes and HLHS in patients.

We thank Reviewer 2 for the thoughtful assessment of our manuscript. Our point-by-point responses to the recommendations are provided (Reviewer 2, “Recommendations for the authors”).

Reviewer #1 (Recommendations for the authors): 

(1) Despite an interesting surveillance model, the disease-causing mechanisms directly downstream of the RP variants remain unclear. Can the authors provide any evidence for abnormal ribosomes or defects in translation in cells harboring such variants? The possibility that reduced translation of cardiac transcription factors such as TBX5 and NKX2-5 may contribute to the functional interactions observed should be considered. How do the authors consider that the RP variants are affecting transcript levels as observed in the study?

Our model implies that cell cycle arrest does not require abnormal ribosomes or translational defects but instead relies on the sensing of RP levels or mutations as a fitness-sensing mechanism that activates TP53/CDKN1A-dependent arrest. Supporting this framework, we observed no significant changes in TBX5 or NKX2-5 expression (data not shown), but rather an upregulation of CDKN1A levels upon RP KD.

(2) The authors suggest that a nucleolar stress program is activated in cells harboring RP gene variants. Can they provide additional evidence for this beyond p53 activation? 

We added additional data to support nucleolar stress (Suppl. Fig. 6) and text (lines 52635):

To determine whether cardiac KD of RpS15Aa causes nucleolar stress in the Drosophila heart, we stained larval hearts for Fibrillarin, a marker for nucleoli and nucleolar integrity.  We found that RpS15Aa KD causes expansion of nucleolar Fibrillarin staining in cardiomyocyte, which is a hallmark of nucleolar stress (Suppl. Fig. 6A-C). As a control, we also performed cardiac KD of Nopp140, which is known to cause nucleolar stress upon loss-of-function. We found a similar expansion of Fibrillarin staining in larval cardiomyocyte nuclei (Suppl. Fig. 6C,D). This suggests that RpS15Aa KD indeed causes nucleolar stress in the Drosophila heart, that likely contributes to the dramatic heart loss in adults.

Other recommendations: 

(3) Concerning the cell type specificity, in the proliferation screen, were similar effects seen on the actinin negative as actinin positive EdU+ cells? It would be helpful to refer to the fibroblast result shown in Supplementary Figure 1C in the results section. 

As suggested by reviewer #1, we have added a reference to Supplementary Fig. 1C, D and noted that RP knockdown exerts a non–CM-specific effect on proliferation.

(4) The authors refer to HLHS patients with atrial septal defects and reduced right ventricular ejection fraction. Please clarify the specificity of the new findings to HLHS versus other forms of CHD, as implied in several places in the manuscript, including the abstract.

This study focused on a cohort of 25 HLHS proband-parent trios selected for poor clinical outcome, including restrictive atrial septal defect and reduced right ventricular ejection fraction.  We have revised the following sentence  in response to the Reviewer’s comment (lines 567-571): “While our study highlights the potential of this approach for gene prioritization, additional research is needed to directly demonstrate the functional consequence of the identified genetic variants, verify an association between RP encoding genes and HLHS in other patient cohorts with and without poor outcome, and determine if RP variants have a broader role in CHD susceptibility.

(5) The multi-model approach taken by the authors is clearly a good system for characterizing disease-causing variants. Did the authors score for cardiomyocyte proliferation or the time of phenotypic onset in the zebrafish model? 

We used an antibody against phosphohistone 3 to identify proliferating cells and DAPI to identify all cardiac cells in control injected, rps15a morphants, and rps15a crispants. We found that  cell numbers and proliferating cells were significantly reduced at 24 and 48 hpf. By 72 hpf cardiac cell proliferation is greatly diminished even in controls, where proliferation typically declines. 

Reduced ventricular cardiomyocyte numbers could potentially result from impaired addition of LTPB3-expressing progenitors. In experiments where altered cardiac rhythm is observed, please comment on the possible links to proliferation.

Heart function data showed that heart period (R-R interval) was unaffected in morphants and crispants at 72 hpf where we also observed significant reductions in cell numbers. This suggests that the bradycardia observed in the rps15a + nkx2.5 or tbx5a double KD (Sup. Fig. 5D & E) was not due to the reduction in cell numbers alone. 

Author response image 1.

Finally, the use of the mouse to model HLHS in potential follow-up studies should be discussed. 

We have added a mouse model comment to the discussion (lines 571-74): “In conclusion, we propose that the approach outlined in this study provides a novel framework for rapidly prioritizing candidate genes and systematically testing them, individually or in combination, using a CRISPR/Cas9 genome-editing strategy in mouse embryos (PMID: 28794185)”.

(6) When the authors scored proliferation in cells from the proband in family 75H, did they validate that RPS15A expression is reduced, consistent with a regulatory region defect? 

Good point. We examined RPS15A expression in these cells and found no significant reduction in gene expression in day 25 cardiomyocytes (data not shown). One possible explanation is that this variant may regulate RPS15A expression in a stage-specific manner during differentiation or under additional stress conditions.

(7) Minor point. Typo on line 494: comma should be placed after KD, not before.

Thank you, this has now been corrected (new line 490)

Reviewer #2 (Recommendations for the authors):  

(1) The authors are invited to revise the part of the manuscript that describes the genetic analysis and provide a more balanced discussion of the WGS data, with a conclusion that aligns with the strength of the human genetic data. 

We disagree with reviewer #2’s assessment. The goal of our study is not to apply a classical genetic approach to establish variant pathogenicity, but rather to employ a multidisciplinary framework to prioritize candidate genes and variants and to examine their roles in heart development using model systems. In this context, genetic analysis serves primarily as a filtering tool rather than as a means of definitively establishing causality.

(2) The genetic analysis of patients does not appear to provide strong evidence for an association between RP gene variants and HLHS. More information regarding methodology and the identified variants is needed. 

HLHS is widely recognized as an oligogenic and heterogeneous genetic disease in which traditional genetic analyses have consistently failed to prioritize any specific gene class as reviewer#2 is pointing out. Therefore, relying solely on genetic analysis is unlikely to yield strong evidence for association with a given gene class. This limitation provides the rationale for our multidisciplinary gene prioritization strategy, which leverages model systems to interrogate candidate gene function. Ultimately, definitive validation of this approach will require studies in relevant in vivo models to establish causality within the context of a four-chambered heart (see also Discussion).

In Table S2, it would be appropriate to provide information on sequence, MAF, and CADD. Please note the source of MAF% (GnomAD version?, which population?).  

As summarized in Figure 2A, the 292 genes from the families with the 25 proband with poor outcome displayed in Supplemental Table 2 fulfilled a comprehensive candidate gene prioritization algorithm based on the variant, gene, inheritance, and enrichment, which required all of the following: 1) variants identified by whole genome sequencing with minor allele frequency <1%; 2) missense, loss-of-function, canonical splice, or promoter variants; 3) upper quartile fetal heart expression; and 4)De novo or recessive inheritance. Unbiased network analysis of these 292 genes, which are displayed in Supplemental Table 2 for completeness, identified statistically significant enrichment of ribosomal proteins. The details about MAF, CADD score, and sequence highlighted by the Reviewer are provided for the RP genes in Table 1, which are central to the focus and findings of the manuscript.    

It would also be helpful for the reader if genome coordinates (e.g., 16-11851493-G-A for RSL1D1 p.A7V) were provided for each variant in both Table 1 and S2.

Genome coordinates have been added to Table 1.

(3) The dataset from the hPSC-CM screen could be of high value for the community. It would be appropriate if the complete dataset were made available in a usable format. 

The dataset from the hPSC-CM screen has been added to the manuscript as Supp Table 1

(4) The "rare predicted-damaging promoter variant in RPS15A" (c.-95G>A) does not appear so rare. Considering the MAF of 0,00662, the frequency of heterozygous carriers of this variant is 1 out of 76 individuals in the general population. Thus, considering the frequency of HLHS in the population (2-3 out of 10,000) and the small size of family 75H, the data do not appear to indicate any association between this particular variant and HLHS. The variants in Table 1 also appear to have relatively mild effects on the gene product, judging from the MAF and CADD scores. The authors are invited to discuss why they find these variants disease-causing in HLHS. 

Our study design is based on the widely held premise that HLHS is an oligogenic disorder. Our multi-model systems platform centered on comprehensive filtering of coding and regulatory variants identified by whole genome sequencing of HLHS probands to identify candidate genes associated with susceptibility to this rare developmental phenotype. 75H proved to be a high-value family for generating a relatively short list of candidate genes for left-sided CHD. Given the rarity of both left-sided CHD and the RPS15A variant identified in the HLHS proband and his 5th degree relative, with a frequency consistent with a risk allele for an oligogenic disorder, we made the reasonable assumption that this was a bona fide genotype-phenotype association rather than a chance occurrence. Moreover, incomplete penetrance and variable expression is consistent with a genetically complex basis of disease whereby the shared variant is risk-conferring and acts in conjunction with additional genetic, epigenetic, and/or environmental factors that lead to a left-sided CHD phenotype. In sum, we do not claim these variants are definitively disease causing, but rather potentially contributing risk factors.

(5) Information is lacking on how clustering of RP genes was demonstrated using STRING (with P-values that support the conclusions). What is meant by "when the highest stringency filter was applied"? Does this refer to the STRING interaction score or something else? The authors could also explain which genes were used to search STRING (e.g., all 292 candidate genes) and provide information on the STRING interaction score used in the analysis, the number of nodes and edges in the network.

To determine whether certain gene networks were over-represented, two online bioinformatics tools were used. First, genes were inputted into STRING (Author response table 2 below) to investigate experimental and predicted protein-protein and genetic interactions. Clustering of ribosomal protein genes was demonstrated when applying the highest stringency filter. Next, genes were analyzed for potential enrichment of genes by ontology classification using PANTHER .Applying Fisher’s exact test and false discovery rate corrections, ribosomal proteins were the most enriched class when compared to the reference proteome, including data annotated by molecular function (4.84-fold, p=0.02), protein class (6.45-fold, p=0.00001), and cellular component (9.50fold, p=0.001). A majority of the identified RP candidate genes harbored variants that fit a recessive inheritance disease model.

Author response image 2.

Author response:

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

Reviewer #1 (Public review): 

“The study analyzes the gastric fluid DNA content identified as a potential biomarker for human gastric cancer. However, the study lacks overall logicality, and several key issues require improvement and clarification. In the opinion of this reviewer, some major revisions are needed:” 

(1) “This manuscript lacks a comparison of gastric cancer patients' stages with PN and N+PD patients, especially T0-T2 patients.”

We are grateful for this astute remark. A comparison of gfDNA concentration among the diagnostic groups indicates a trend of increasing values as the diagnosis progresses toward malignancy. The observed values for the diagnostic groups are as follows:

Author response table 1.

The chart below presents the statistical analyses of the same diagnostic/tumor-stage groups (One-Way ANOVA followed by Tukey’s multiple comparison tests). It shows that gastric fluid gfDNA concentrations gradually increase with malignant progression. We observed that the initial tumor stages (T0 to T2) exhibit intermediate gfDNA levels, which in this group is significantly lower than in advanced disease (p = 0.0036), but not statistically different from non-neoplastic disease (p = 0.74).

Author response image 1.

(2) “The comparison between gastric cancer stages seems only to reveal the difference between T3 patients and early-stage gastric cancer patients, which raises doubts about the authenticity of the previous differences between gastric cancer patients and normal patients, whether it is only due to the higher number of T3 patients.”

We appreciate the attention to detail regarding the numbers analyzed in the manuscript. Importantly, the results are meaningful because the number of subjects in each group is comparable (T0-T2, N = 65; T3, N = 91; T4, N = 63). The mean gastric fluid gfDNA values (ng/µL) increase with disease stage (T0-T2: 15.12; T3-T4: 30.75), and both are higher than the mean gfDNA values observed in non-neoplastic disease (10.81 ng/µL for N+PD and 10.10 ng/µL for PN). These subject numbers in each diagnostic group accurately reflect real-world data from a tertiary cancer center.

(3) “The prognosis evaluation is too simplistic, only considering staging factors, without taking into account other factors such as tumor pathology and the time from onset to tumor detection.”

Histopathological analyses were performed throughout the study not only for the initial diagnosis of tissue biopsies, but also for the classification of Lauren’s subtypes, tumor staging, and the assessment of the presence and extent of immune cell infiltrates. Regarding the time of disease onset, this variable is inherently unknown--by definition--at the time of a diagnostic EGD. While the prognosis definition is indeed straightforward, we believe that a simple, cost-effective, and practical approach is advantageous for patients across diverse clinical settings and is more likely to be effectively integrated into routine EGD practice.

(4) “The comparison between gfDNA and conventional pathological examination methods should be mentioned, reflecting advantages such as accuracy and patient comfort. “

We wish to reinforce that EGD, along with conventional histopathology, remains the gold standard for gastric cancer evaluation. EGD under sedation is routinely performed for diagnosis, and the collection of gastric fluids for gfDNA evaluation does not affect patient comfort. Thus, while gfDNA analysis was evidently not intended as a diagnostic EGD and biopsy replacement, it may provide added prognostic value to this exam.

(5) “There are many questions in the figures and tables. Please match the Title, Figure legends, Footnote, Alphabetic order, etc. “

We are grateful for these comments and apologize for the clerical oversight. All figures, tables, titles and figure legends have now been double-checked.

(6) “The overall logicality of the manuscript is not rigorous enough, with few discussion factors, and cannot represent the conclusions drawn. “

We assume that the unusual wording remark regarding “overall logicality” pertains to the rationale and/or reasoning of this investigational study. Our working hypothesis was that during neoplastic disease progression, tumor cells continuously proliferate and, depending on various factors, attract immune cell infiltrates. Consequently, both tumor cells and immune cells (as well as tumor-derived DNA) are released into the fluids surrounding the tumor at its various locations, including blood, urine, saliva, gastric fluids, and others. Thus, increases in DNA levels within some of these fluids have been documented and are clinically meaningful. The concurrent observation of elevated gastric fluid gfDNA levels and immune cell infiltration supports the hypothesis that increased gfDNA—which may originate not only from tumor cells but also from immune cells—could be associated with better prognosis, as suggested by this study of a large real-world patient cohort.

In summary, we thank Reviewer #1 for his time and effort in a constructive critique of our work.

Reviewer #2 (Public review):

Summary: 

“The authors investigated whether the total DNA concentration in gastric fluid (gfDNA), collected via routine esophagogastroduodenoscopy (EGD), could serve as a diagnostic and prognostic biomarker for gastric cancer. In a large patient cohort (initial n=1,056; analyzed n=941), they found that gfDNA levels were significantly higher in gastric cancer patients compared to non-cancer, gastritis, and precancerous lesion groups. Unexpectedly, higher gfDNA concentrations were also significantly associated with better survival prognosis and positively correlated with immune cell infiltration. The authors proposed that gfDNA may reflect both tumor burden and immune activity, potentially serving as a cost-effective and convenient liquid biopsy tool to assist in gastric cancer diagnosis, staging, and follow-up.”

Strengths: 

“This study is supported by a robust sample size (n=941) with clear patient classification, enabling reliable statistical analysis. It employs a simple, low-threshold method for measuring total gfDNA, making it suitable for large-scale clinical use. Clinical confounders, including age, sex, BMI, gastric fluid pH, and PPI use, were systematically controlled. The findings demonstrate both diagnostic and prognostic value of gfDNA, as its concentration can help distinguish gastric cancer patients and correlates with tumor progression and survival. Additionally, preliminary mechanistic data reveal a significant association between elevated gfDNA levels and increased immune cell infiltration in tumors (p=0.001).”

Reviewer #2 has conceptually grasped the overall rationale of the study quite well, and we are grateful for their assessment and comprehensive summary of our findings.

Weaknesses: 

(1) “The study has several notable weaknesses. The association between high gfDNA levels and better survival contradicts conventional expectations and raises concerns about the biological interpretation of the findings.“

We agree that this would be the case if the gfDNA was derived solely from tumor cells. However, the findings presented here suggest that a fraction of this DNA would be indeed derived from infiltrating immune cells. The precise determination of the origin of this increased gfDNA remains to be achieved in future follow-up studies, and these are planned to be evaluated soon, by applying DNA- and RNA-sequencing methodologies and deconvolution analyses.

(2) “The diagnostic performance of gfDNA alone was only moderate, and the study did not explore potential improvements through combination with established biomarkers. Methodological limitations include a lack of control for pre-analytical variables, the absence of longitudinal data, and imbalanced group sizes, which may affect the robustness and generalizability of the results.“

Reviewer #2 is correct that this investigational study was not designed to assess the diagnostic potential of gfDNA. Instead, its primary contribution is to provide useful prognostic information. In this regard, we have not yet explored combining gfDNA with other clinically well-established diagnostic biomarkers. We do acknowledge this current limitation as a logical follow-up that must be investigated in the near future.

Moreover, we collected a substantial number of pre-analytical variables within the limitations of a study involving over 1,000 subjects. Longitudinal samples and data were not analyzed here, as our aim was to evaluate prognostic value at diagnosis. Although the groups are imbalanced, this accurately reflects the real-world population of a large endoscopy center within a dedicated cancer facility. Subjects were invited to participate and enter the study before sedation for the diagnostic EGD procedure; thus, samples were collected prospectively from all consenting individuals.

Finally, to maintain a large, unbiased cohort, we did not attempt to balance the groups, allowing analysis of samples and data from all patients with compatible diagnoses (please see Results: Patient groups and diagnoses).

(3) “Additionally, key methodological details were insufficiently reported, and the ROC analysis lacked comprehensive performance metrics, limiting the study's clinical applicability.“

We are grateful for this useful suggestion. In the current version, each ROC curve (Supplementary Figures 1A and 1B) now includes the top 10 gfDNA thresholds, along with their corresponding sensitivity and specificity values (please see Suppl. Table 1). The thresholds are ordered from-best-to-worst based on the classic Youden’s J statistic, as follows:

Youden Index = specificity + sensitivity – 1 [Youden WJ. Index for rating diagnostic tests. Cancer 3:32-35, 1950. PMID: 15405679]. We have made an effort to provide all the key methodological details requested, but we would be glad to add further information upon specific request.

Reviewer #1 (Recommendations for the authors):

The authors should pay attention to ensuring uniformity in the format of all cited references, such as the number of authors for each reference, the journal names, publication years, volume numbers, and page number formats, to the best extent possible. 

Thank you for pointing this inconsistency. All cited references have now been revisited and adjusted properly. We apologize for this clerical oversight.

Reviewer #2 (Recommendations for the authors):

(1) “High gfDNA levels were surprisingly linked to better survival, which conflicts with the conventional understanding of cfDNA as a tumor burden marker. Was any qualitative analysis performed to distinguish DNA derived from immune cells versus tumor cells?“

Tumor-derived DNA is certainly present in gfDNA, as our group has unequivocally demonstrated in a previous publication [Pizzi M. P., et al. (2019) Identification of DNA mutations in gastric washes from gastric adenocarcinoma patients: Possible implications for liquid biopsies and patient follow-up Int J Cancer 145:1090–1097. DOI: 10.1002/ijc.32114]. However, in the present manuscript, our data suggest that gfDNA may also contain DNA derived from infiltrating immune cells. This may also be the case for other malignancies, and qualitative deconvolution studies could provide more informative information. To achieve this, DNA sequencing and RNA-Seq analyses may offer relevant evidence. Our study should be viewed as an original and preliminary analysis that may encourage such quantitative and qualitative studies in biofluids from cancer patients. Currently, this is a simple approach (which might be its essential beauty), but we hope to investigate this aspect further in future studies.

(2) “The ROC curve AUC was 0.66, indicating only moderate discrimination ability. Did the authors consider combining gfDNA with markers such as CEA or CA19-9 to improve diagnostic accuracy?“

This is indeed a logical idea, which shall certainly be explored in planned follow-up studies.

(3) “DNA concentration could be influenced by non-biological factors, including gastric fluid pH, sampling location, time delay, or freeze-thaw cycles. Were these operational variables assessed for their effect on data stability?“

We appreciate the rigor of the evaluation. Yes, information regarding gastric fluid pH was collected. All samples were collected from the stomach during EGD procedure. Samples were divided in aliquots and were thawed only once. This information is now provided in the updated manuscript text.

(4) “This cross-sectional study lacks data on gfDNA changes over time, limiting conclusions on its utility for monitoring treatment response or predicting recurrence.“

Again, temporal evaluation is another excellent point, and it will be the subject of future analyses. In this exploratory study, samples were collected at diagnosis, at a single point. We have not obtained serial samples, as participants received appropriate therapy soon following diagnosis.

(5) The normal endoscopy group included only 10 patients, the precancerous lesion group 99 patients, while the gastritis group had 596 patients. Such uneven sample sizes may affect statistical reliability and generalizability. Has weighted analysis or optimized sampling been considered for future studies?“

Yes, in future studies this analysis will be considered, probably by employing stratified random sampling with relevant patient attributes recorded.

(6) “The SciScore was only 2 points, indicating that key methodological details such as inclusion/exclusion criteria, randomization, sex variables, and power calculation were not clearly described. It is recommended that these basic research elements be supplemented in the Methods section. “

This was an exploratory research, the first of its kind, to evaluate prognostic potential of gfDNA in the context of gastric cancer. Patients were not included if they did not sign the informed consent or excluded if they withdrew after consenting. Other exclusion criteria included diagnoses of conditions such as previous gastrectomy or esophagectomy, or the presence of non-gastric malignancies. Randomization and power analyses were not applicable, as no prior data were available regarding gfDNA concentration values or its diagnostic/prognostic potential. All subjects, regardless of sex, were invited to participate without discrimination or selection.

(7) “Although a ROC curve was provided in the supplementary materials (Supplementary Figure 1), only the curve and AUC value were shown without sensitivity, specificity, predictive values, or cutoff thresholds. The authors are advised to provide a full ROC performance assessment to strengthen the study's clinical relevance.

These data are now given alongside the ROC curves in the Supplementary Information section, specifically in Supplementary Figure 1 and in the newly added Supplementary Table 1.

We thank Reviewer #2 for an insightful and positive overall assessment of our work.

Author response:

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

Reviewer #1 (Public review):

This manuscript reports a dual-task experiment intended to test whether language prediction relies on executive resources, using surprisal-based measures of predictability and an n-back task to manipulate cognitive load. While the study addresses a question under debate, the current design and modeling framework fall short of supporting the central claims. Key components of cognitive load, such as task switching, word prediction vs integration, are not adequately modeled. Moreover, the weak consistency in replication undermines the robustness of the reported findings. Below unpacks each point. 

Cognitive load is a broad term. In the present study, it can be at least decomposed into the following components: 

(1)  Working memory (WM) load: news, color, and rank. 

(2)  Task switching load: domain of attention (color vs semantics), sensorimotor rules (c/m vs space).

(3)  Word comprehension load (hypothesized against): prediction, integration. 

The components of task switching load should be directly included in the statistical models. Switching of sensorimotor rules may be captured by the "n-back reaction" (binary) predictor. However, the switching of attended domains and the interaction between domain switching and rule complexity (1-back or 2-back) were not included. The attention control experiment (1) avoided useful statistical variation from the Read Only task, and (2) did not address interactions. More fundamentally, task-switching components should be directly modeled in both performance and full RT models to minimize selection bias. This principle also applies to other confounding factors, such as education level. While missing these important predictors, the current models have an abundance of predictors that are not so well motivated (see later comments). In sum, with the current models, one cannot determine whether the reduced performance or prolonged RT was due to affecting word prediction load (if it exists) or merely affecting the task switching load. 

The entropy and surprisal need to be more clearly interpreted and modeled in the context of the word comprehension process. The entropy concerns the "prediction" part of the word comprehension (before seeing the next word), whereas surprisal concerns the "integration" part as a posterior. This interpretation is similar to the authors writing in the Introduction that "Graded language predictions necessitate the active generation of hypotheses on upcoming words as well as the integration of prediction errors to inform future predictions [1,5]." However, the Results of this study largely ignored entropy (treating it as a fixed effect) and only focus on surprisal without clear justification. 

In Table S3, with original and replicated model fitting results, the only consistent interaction is surprisal x age x cognitive load [2-back vs. Reading Only]. None of the two-way interactions can be replicated. This is puzzling and undermines the robustness of the main claims of this paper. 

Reviewer #2 (Public review):

Summary

This paper considers the effects of cognitive load (using an n-back task related to font color), predictability, and age on reading times in two experiments. There were main effects of all predictors, but more interesting effects of load and age on predictability. The effect of load is very interesting, but the manipulation of age is problematic, because we don't know what is predictable for different participants (in relation to their age). There are some theoretical concerns about prediction and predictability, and a need to address literature (reading time, visual world, ERP studies). 

Strengths/weaknesses 

It is important to be clear that predictability is not the same as prediction. A predictable word is processed faster than an unpredictable word (something that has been known since the 1970/80s), e.g., Rayner, Schwanenfluegel, etc. But this could be due to ease of integration. I think this issue can probably be dealt with by careful writing (see point on line 18 below). To be clear, I do not believe that the effects reported here are due to integration alone (i.e., that nothing happens before the target word), but the evidence for this claim must come from actual demonstrations of prediction. 

The effect of load on the effects of predictability is very interesting (and also, I note that the fairly novel way of assessing load is itself valuable). Assuming that the experiments do measure prediction, it suggests that they are not cost-free, as is sometimes assumed. I think the researchers need to look closely at the visual world literature, most particularly the work of Huettig. (There is an isolated reference to Ito et al., but this is one of a large and highly relevant set of papers.) 

There is a major concern about the effects of age. See the Results (161-5): this depends on what is meant by word predictability. It's correct if it means the predictability in the corpus. But it may or may not be correct if it refers to how predictable a word is to an individual participant. The texts are unlikely to be equally predictable to different participants, and in particular to younger vs. older participants, because of their different experiences. To put it informally, the newspaper articles may be more geared to the expectations of younger people. But there is also another problem: the LLM may have learned on the basis of language that has largely been produced by young people, and so its predictions are based on what young people are likely to say. Both of these possibilities strike me as extremely likely. So it may be that older adults are affected more by words that they find surprising, but it is also possible that the texts are not what they expect, or the LLM predictions from the text are not the ones that they would make. In sum, I am not convinced that the authors can say anything about the effects of age unless they can determine what is predictable for different ages of participants. I suspect that this failure to control is an endemic problem in the literature on aging and language processing and needs to be systematically addressed. 

Overall, I think the paper makes enough of a contribution with respect to load to be useful to the literature. But for discussion of age, we would need something like evidence of how younger and older adults would complete these texts (on a word-by-word basis) and that they were equally predictable for different ages. I assume there are ways to get LLMs to emulate different participant groups, but I doubt that we could be confident about their accuracy without a lot of testing. But without something like this, I think making claims about age would be quite misleading. 

We thank both reviewers for their constructive feedback and for highlighting areas where our theoretical framing and analyses could be clarified and strengthened. We have carefully considered each of the points raised and made substantial additions and revisions.

As a summary, we have directly addressed the concerns raised by the reviewers by incorporating task-switching predictors into the statistical models, paralleling our focus on surprisal with a full analysis and interpretation of entropy, clarifying the robustness (and limitations) of the replicated findings, and addressing potential limitations in our Discussion.

We believe these revisions substantially strengthen the manuscript and improve the reading flow, while also clarifying the scope of our conclusions. We will not illustrate these changes in more detail:

(1) Cognitive load and task-switching components.

We agree that cognitive load is a multifaceted construct, particularly since our secondary task broadly targets executive functioning. In response to Reviewer 1, we therefore examined task-switching demands more closely by adding the interaction term n-back reaction × cognitive load to a model restricted to 1-back and 2-back Dual Task blocks (as there were no n-back reactions in the Reading Only condition). This analysis showed significantly longer reading times in the 2-back than in the 1back condition, both for trials with and without an n-back reaction. Interestingly, the difference between reaction and no-reaction trials was smaller in the 2-back condition (β = -0.132, t(188066.09) = -34.269, p < 0.001), which may simply reflect the general increase in reading time for all trials so that the effect of the button press time decreases in comparison to the 1-back. In that sense, these findings are not unexpected and largely mirror the main effect of cognitive load. Crucially, however, the three-way interaction of cognitive load, age, and surprisal remained robust (β = 0.00004, t(188198.86) = 3.540, p < 0.001), indicating that our effects cannot be explained by differences in taskswitching costs across load conditions. To maintain a streamlined presentation, we opted not to include this supplementary analysis in the manuscript.

(2) Entropy analyses.

Reviewer 1 pointed out that our initial manuscript placed more emphasis on surprisal. In the revised manuscript, we now report a full set of entropy analyses in the supplementary material. In brief, these analyses show that participants generally benefit from lower entropy across cognitive load conditions, with one notable exception: young adults in the Reading Only condition, where higher entropy was associated with faster reading times. We have added these results to the manuscript to provide a more complete picture of the prediction versus integration distinction highlighted in the review (see sections “Control Analysis: Disentangling the Effect of Cognitive Load on Pre- and PostStimulus Predictive Processing” in the Methods and “Disentangling the Effect of Cognitive Load on Pre- and Post-Stimulus Predictive Processing“ in the Results).

(3) Replication consistency.

Reviewer 1 noted that the results of the replication analysis were somewhat puzzling. We take this point seriously and agree that the original model was likely underpowered to detect the effect of interest. To address this, we excluded the higher-level three-way interaction of age, cognitive load, and surprisal, focusing instead on the primary effect examined in this paper: the modulatory influence of cognitive load on surprisal. Using this approach, we observed highly consistent results between the original online subsample and the online replication sample.

(4) Potential age bias in GPT-2.  

We thank Reviewer 2 for their thoughtful and constructive feedback and agree that a potential age bias in GPT-2’s next-token predictions warrants caution. We thus added a section in the Discussion explicitly considering this limitation, and explain why it should not affect the implications of our study.

Reviewer #1 (Recommendations for the authors):

The d-prime model operates at the block level. How many observation goes into the fitting (about 175*8=1050)? How can the degrees of freedom of a certain variable go up to 188435? 

We thank the reviewer for spotting this issue. Indeed, there was an error in our initial calculations, which we have now corrected in the manuscript. Importantly, the correction does not meaningfully affect the results for the analysis of d-primes or the conclusions of the study (see line 102).  

“A linear mixed-effects model revealed n-back performance declined with cognitive load (β = -1.636, t(173.13) = -26.120, p < 0.001), with more pronounced effects with advancing age (β = -0.014, t(169.77) = -3.931, p > 0.001; Fig. 3b, Table S1)”.

Consider spelling out all the "simple coding schemes" explicitly. 

We thank the reviewer for this helpful suggestion. In the revised manuscript, we have now included the modelled contrasts in brackets after each predictor variable.

“Example from line 527: In both models, we included recording location (online vs. lab), cognitive load (1-back and 2back Dual Task vs. Reading Only as the reference level) and continuously measured age (centred) in both models as well as the interaction of age and cognitive load as fixed effects”.

The relationship between comprehension accuracy and strategies for color judgement is unclear or not intuitive. 

We thank the reviewer for this helpful comment. The n-back task, which required participants to judge colours, was administered at the single-trial level, with colours pseudorandomised to prevent any specific colour - or sequence of colours - from occurring more frequently than others. In contrast, comprehension questions were presented at the end of each block, meaning that trial-level stimulus colour was unrelated to accuracy on the block-level comprehension questions. However, we agree that this distinction may not have been entirely clear, and we have now added a brief clarification in the Methods section to address this point (see line 534):  

“Please note that we did not control for trial-level stimulus colour here. The n-back task, which required participants to judge colours, was administered at the single-trial level, with colours pseudorandomised to prevent any specific colour - or sequence of colours - from occurring more frequently than others. In contrast, comprehension questions were presented at the end of each block, meaning that trial-level stimulus colour was unrelated to accuracy on the blocklevel comprehension questions”.

Could you explain why comprehension accuracy is not modeled in the same way as d-prime, i.e., with a similar set of predictors? 

This is a very good point. After each block, participants answered three comprehension questions that were intentionally designed to be easy: they could all be answered correctly after having read the corresponding text, but not by common knowledge alone. The purpose of these questions was primarily to ensure participants paid attention to the texts and to allow exclusion of participants who failed to understand the material even under minimal cognitive load. As comprehension accuracy was modelled at the block level with 3 questions per block, participants could achieve only discrete scores of 0%, 33.3%, 66.7%, or 100%. Most participants showed uniformly high accuracy across blocks, as expected if the comprehension task fulfilled its purpose. However, this limited variance in performance caused convergence issues when fitting a comprehension-accuracy model at the same level of complexity as the d′ model. To model comprehension accuracy nonetheless, we therefore opted for a reduced model complexity in this analysis.

RT of previous word: The motivations described in the Methods, such as post-error-slowing and sequential modulation effects, lack supporting evidence. The actual scope of what this variable may account for is unclear.  

We are happy to elaborate further regarding the inclusion of this predictor. Reading times, like many sequential behavioral measures, exhibit strong autocorrelation (Schuckart et al., 2025, doi: 10.1101/2025.08.19.670092). That is, the reading time of a given word is partially predictable from the reading time of the previous word(s). Such spillover effects can confound attempts to isolate trialspecific cognitive processes. As our primary goal was to model single-word prediction, we explicitly accounted for this autocorrelation by including the log reading time of the preceding trial as a covariate. This approach removes variance attributable to prior behavior, ensuring that the estimated effects reflect the influence of surprisal and cognitive load on the current word, rather than residual effects of preceding trials. We now added this explanation to the manuscript (see line 553):

“Additionally, it is important to consider that reading times, like many sequential behavioural measures, exhibit strong autocorrelation (Schuckart et al., 2025), meaning that the reading time of a given word is partially predictable from the reading time of the previous word. Such spillover effects can confound attempts to isolate trial-specific cognitive processes. As our primary goal was to model single-word prediction, we explicitly accounted for this autocorrelation by including the reading time of the preceding trial as a covariate”.  

Block-level d-prime: It was shown with the d-prime performance model that block-level d-prime is a function of many of the reading-related variables. Therefore, it is not justified to use them here as "a proxy of each participant's working memory capacity."

We thank the reviewer for their comment. We would like to clarify that the d-prime performance model indeed included only dual-task d-primes (i.e., d-primes obtained while participants were simultaneously performing the reading task). In contrast, the predictor in question is based on singletask d-primes, which are derived from the n-back task performed in isolation. While dual- and singletask d-primes may be correlated, they capture different sources of variance, justifying the use of single-task d-primes here as a measure of each participant’s working memory capacity.

Word frequency is entangled with entropy and surprisal. Suggest removal.

We appreciate the reviewer’s comment. While word frequency is correlated with word surprisal, its inclusion does not affect the interpretation of the other predictors and does not introduce any bias. Moreover, it is a theoretically important control variable in reading research. Since we are interested in the effects of surprisal and entropy beyond potential biases through word length and frequency, we believe these are important control variables in our model. Moreover, checks for collinearity confirmed that word frequency was neither strongly correlated with surprisal nor entropy. In this sense, including it is largely pro forma: it neither harms the model nor materially changes the results, but it ensures that the analysis appropriately accounts for a well-established influence on word processing.

Entropy reflects the cognitive load of word prediction. It should be investigated in parallel and with similar depth as surprisal (which reflects the load of integration).

This is an excellent point that warrants further investigation, especially since the previous literature on the effects of entropy on reading time is scarce and somewhat contradictory. We have thus added additional analyses and now report the effects of cognitive load, entropy, and age on reading time (see sections “Disentangling the Effect of Cognitive Load on Pre- and Post-Stimulus Predictive Processing” in the Results, “Control Analysis: Disentangling the Effect of Cognitive Load on Pre- and Post-Stimulus Predictive Processing” in the Methods as well as Fig. S7 and Table S6 in the Supplements for full results). In brief, we observe a significant three-way interaction among age, cognitive load, and entropy. Specifically, while all participants benefit from low entropy under high cognitive load, reflected by shorter reading times, in the baseline condition this benefit is observed only in older adults. Interestingly, in the baseline condition with minimal cognitive load, younger adults even show a benefit from high entropy. Thus, although the overall pattern for entropy partly mirrors that for surprisal – older adults showing increased reading times when word entropy is high and generally greater sensitivity to entropy variations – the effects differ in one important respect. Unlike for surprisal, the detrimental impact of increased word entropy is more pronounced under high cognitive load across all participants.

Reviewer #2 (Recommendations for the authors):

I agree in relation to prediction/load, but I am concerned (actually very concerned) that prediction needs to be assessed with respect to age. I suspect this is one reason why there is so much inconsistency in the effects of age in prediction and, indeed, comprehension more generally. I think the authors should either deal with it appropriately or drop it from the manuscript.

Thank you for raising this important concern. It is true that prediction is a highly individual, complex process as it depends upon the experiences a person has made with language over their lifespan. As such, one-size-fits-all approaches are not sufficient to model predictive processing. In our study, we thus took particular care to ensure that our analyses captured both age-related and other interindividual variability in predictive processing.

First, in our statistical models, we included age not only as a nuisance regressor, but also assessed age-related effects in the interplay of surprisal and cognitive load. By doing so, we explicitly model potential age-related differences in how individuals of different ages predict language under different levels of cognitive load.

Second, we hypothesised that predictive processing might also be influenced by a range of interindividual factors beyond age, including language exposure, cognitive ability, and more transient states such as fatigue. To capture such variability, all models included by-subject random intercepts and slopes, ensuring that unmodelled individual differences were statistically accommodated.

Together, these steps allow us to account for both systematic age-related differences and residual individual variability in predictive processing. We are therefore confident that our findings are not confounded by unmodelled age-related variability.

Line 18, do not confuse prediction (or pre-activation) with predictability. Predictability effects can be due to integration difficulty. See Pickering and Gambi 2018 for discussion. The discussion then focuses on graded parallel predictions, but there is also a literature concerned with the prediction of one word, typically using the "visual world" paradigm (which is barely cited - Reference 60 is an exception). In the next paragraph, I would recommend discussing the N400 literature (particularly Federmeier). There are a number of reading time studies that investigate whether there is a cost to a disconfirmed prediction - often finding no cost (e.g., Frisson, 2017, JML), though there is some controversy and apparent differences between ERP and eye-tracking studies (e.g., Staub). This literature should be addressed. In general, I appreciate the value of a short introduction, but it does seem too focused on neuroscience rather than the very long tradition of behavioural work on prediction and predictability.

We thank the reviewer for this suggestion. In the revised manuscript, we have clarified the relevant section of the introduction to avoid confusion between predictability and predictive processing, thereby improving conceptual clarity (see line 16).

“Instead, linguistic features are thought to be pre-activated broadly rather than following an all-or-nothing principle, as there is evidence for predictive processing even for moderately- or low-restraint contexts (Boston et al., 2008; Roland et al., 2012; Schmitt et al., 2021; Smith & Levy, 2013)”.  

We also appreciate the reviewer’s comment regarding the introduction. While our study is behavioural, we frame it in a neuroscience context because our findings have direct implications for understanding neural mechanisms of predictive processing and cognitive load. We believe that this framing is important for situating our results within the broader literature and highlighting their relevance for future neuroscience research.

I don't think 2 two-word context is enough to get good indicators of predictability. Obviously, almost anything can follow "in the", but the larger context about parrots presumably gives a lot more information. This seems to me to be a serious concern - or am I misinterpreting what was done? 

This is a very important point and we thank the reviewer for raising it. Our goal was to generate word surprisal scores that closely approximate human language predictions. In the manuscript, we report analyses using a 2-word context window, following recommendations by Kuribayashi et al. (2022).

To evaluate the impact of context length, we also tested longer windows of up to 60 words (not reported). While previous work (Goldstein et al., 2022) shows that GPT-2 predictions can become more human-like with longer context windows, we found that in our stimuli – short newspaper articles of only 300 words – surprisal scores from longer contexts were highly correlated with the 2word context, and the overall pattern of results remained unchanged. To illustrate, surprisal scores generated with a 10-word context window and surprisal scores generated with the 2-word context window we used in our analyses correlated with Spearman’s ρ = 0.976.

Additionally, on a more technical note, using longer context windows reduces the number of analysable trials, since surprisal cannot be computed for the first k words of a text with a k-word context window (e.g., a 50-word context would exclude ~17% of the data).  

Importantly, while a short 2-word context window may introduce additional noise in the surprisal estimates, this would only bias effects toward zero, making our analyses conservative rather than inflating them. Critically, the observed effects remain robust despite this conservative estimate, supporting the validity of our findings.

However, we agree that this is a particularly important and sensitive point, and have now added a discussion of it to the manuscript (see line 476).

“Entropy and surprisal scores were estimated using a two-word context window. While short contexts have been shown to enhance GPT-2’s psychometric alignment with human predictions, making next-word predictions more human-like (Kuribayashi et al., 2022), other work suggests that longer contexts can also increase model–human similarity (Goldstein et al., 2022). To reconcile these findings in our stimuli and guide the choice of context length, we tested longer windows and found surprisal scores were highly correlated with the 2-word context (e.g., 10-word vs. 2-word context: Spearman’s ρ = 0.976), with the overall pattern of results unchanged. Additionally, employing longer context windows would have also reduced the number of analysable trials, since surprisal cannot be computed for the first k words of a text with a k-word context window. Crucially, any additional noise introduced by the short context biases effect estimates toward zero, making our analyses conservative rather than inflating them”.

Line 92, task performance, are there interactions? Interactions would fit with the experimental hypotheses. 

Yes, we did include an interaction term of age and cognitive load and found significant effects on nback task performance (d-primes; b = -0.014, t(169.8) = -3.913, p < 0.001), but not on comprehension question accuracy (see table S1 and Fig. S2 in the supplementary material).

Line 149, what were these values?

We found surprisal values ranged between 3.56 and 72.19. We added this information in the manuscript (see line 143).

Author response:

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

We thank the reviewers for their comments on the initial submission, which helped us improve and extend the paper. We would like to respond specifically to reviewer #1.

We disagree with the broad criticism of this study as being “almost entirely observational” and lacking “detailed molecular investigation”. We report structures and binding data, show mechanistic detail, identify critical residues and structural features underlying biological activity, and present biologically meaningful data demonstrating a role of the interaction of the M3 protein with collagens. We disagree that insufficient details or controls are included. We agree that our report has limitations, such as an understanding of potential emm1 strain binding to collagen, which might play a role in host tissue colonization, but not in biofilm.

In response to issues raised in the initial review, we conducted several new experiments for the revised manuscript. We believe these strengthen what we report. Firstly, as the reviewer suggested, we conducted a binding experiment where the tertiary fold of M3-NTD was disrupted to confirm the T-shaped fold is indeed required for binding to collagen, as might be expected based on the crystal structure of the complex. To achieve this, we did not, as the reviewer states, use denatured protein in the ITC binding experiment. Instead, we used a monomeric form of M3-NTD, which does not adopt a well-defined tertiary structure, but retains all residues in the context of alpha helices. Secondly, we added more evidence for the importance of structural features (amino acid side chains defining the collagen binding site) by analysing the role of Trp103. Together, we provide clear evidence for the specific role of the T-shaped fold of M3-NTD for collagen binding.

Responding to a constructive criticism by reviewer #1 we characterised M3-NTD mutants to demonstrate conservation of overall structure. NMR is an exquisite tool for this as it is highly sensitive to structural changes. It is not clear why the reviewer suggested we should have measured the stability of the proteins, which is irrelevant here. What matters is that the fold is conserved between mutated variants at the chosen experimental temperature (now added to the Methods section), which NMR demonstrates.

We added errors for the ITC-derived dissociation constants.

In the submitted versions of the paper we did not include the negative control requested by reviewer #1 for experiments shown in Figure 10 - figure supplement 1B. In our view this does not add information supporting our findings. However, we have now added two negative controls, staining of emm1 and emm28 strains. As expected, no reactivity was found with the type-specific M3 HVR antiserum while the M3 BCW antiserum showed weak reactivity, in line with some sequence similarity of the C-terminal regions of M proteins.

Table 2 contains essential information, in line with what generally is shown in crystallographic tables in this journal. All other information can be found in the depositions of our data at the PDB. The structures have been scrutinised and checked by the PDB and passed all quality tests.

We stated how many times experiments were done where appropriate. We now added this information for CLC assays (as given in the previously published protocol, refs. 45, 47). ITC was carried out more than once for optimization but the results of single experiments are shown (as is common practice).

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

Many thanks for assessing our submission. We are grateful for the reviews that have informed a revised version of the paper, which includes additional data and modified text to take into account the reviewers’ comments. 

We addressed the major limitation identified by Reviewer #1 by including data to demonstrate that collagen binding is indeed dependent on the T-shaped fold (major issue 1). Reviewer #1 suggested this needs to be done through extensive mutational work. This in our view was neither feasible nor necessary. Instead, we used ITC to measure collagen peptide binding using a monomeric form of M3, which preserves all residues including the ones involved in binding, but cannot form the T-shaped structure. This achieves the same as unravelling the T fold through mutations, but without the risk of aJecting binding through altering residues that are involved in both binding and definition of the T fold. The experiment shows a very weak interaction, confirming the fold of the M3-NTD is required for binding activity.

Reviewer #1 finds the study limited for being “almost entirely observational”. Structural biology is by its nature observational, which is not a limitation but the very purpose of this approach. Our study goes beyond observing structures. In the first version of our paper, we identified a critical residue within a previously mapped binding site, and demonstrated through mutagenesis a causal link between presence of this residue on a tertiary fold and collagen binding activity. However, we agree this analysis could have been strengthened by additional mutagenesis, which we carried out and describe in the revised manuscript. This identifies a second residue that is critical for collagen binding. We firmed up these mutational experiments with a characterisation of mutated forms of M3 by NMR spectroscopy to confirm that these mutations did not aJect the overall fold, addressing major issue no. 2 of reviewer #1. We further demonstrate that the interaction between M3 and collagen is the cause of greatly enhanced biofilm formation as observed in patient biopsies and a tissue model of infection. We show that other streptococci that do not possess a surface protein presenting collagen binding sites like M3 do not form collagen-dependent biofilm. We therefore do not think that criticising our study for being almost entirely observational is valid. 

Major issue 3:

We agree with the reviewer that it would be useful to carry out experiments with k.o. and complemented strains. Such experiments go beyond the scope of our study, but might be carried out by us or others in the future. We disagree that emm1 is used “as a negative”. Instead, we established that, in contrast to emm3 strains, emm1 strain biofilm formation is not enhanced by collagen. 

We addressed major issue 4 by quantifying colocalizations in the patient biopsies and 3D tissue model experiments.

We thank Reviewer #2 for the thorough analysis of our reported findings. The main criticism here (issue 1) concerns the question of whether binding of emm3 streptococci would diJer to diJerent types of collagen. Our collagen peptide binding assays together with the structural data identify the collagen triple helix as the binding site for M3. While collagen types diJer in their distribution, functions and morphology in diJerent tissues, they all have in common triple-helical (COL) regions with high sequence similarity that are non-specifically recognised by M3. Therefore, our data in conjunction with the body of published work showing binding to M3 to collagens I, II, III and IV suggest it is highly likely that emm3 streptococci will indeed bind to all types of collagen in the same manner. We added a statement to the manuscript to make this point more clearly. We also added a prediction of a complex between M3 and a collagen I triple-helical peptide, which supports the idea of conserved binding mechanism for all collagen types. Whether this means all collagen types in the various tissues where they occur are targeted by emm3 streptococci is a very interesting question, however one that goes beyond the scope of our study.

Minor issues identified by the reviewers were addressed through changes in the text and addition of figures.

Summary of changes:

(1) Two new authors have been added due to inclusion of additional data and analysis.

(2) New experimental data included in section "M3-NTD harbors the collagen binding site".

(3) Figure 3 panels A and B assigned and swapped.

(4) Figure 4 changed to include new data and move mutant M3-NTD ITC graphs to supplement.

(5) Table 2 corrected and amended.

(6) AlphaFold3 quality parameters ipTM and pTM added to all figures showing predicted structures.

(7) New supplementary figure added showing crystal packing of M3-NTD/collagen peptide complex.

(8) Figure supplement of predicted M-protein/collagen peptide complexes includes new panel for a type I collagen peptide bound to M3.

(9) New figure supplement showing mutant M3-NTD ITC data.

(10) New figure supplement showing 1D ¹H NMR spectra of M3-NTD mutants.

(11) Included data for additional M3-NTD mutants assessing role of Trp103 in collagen binding. Text extended to describe and place into context findings from ITC binding studies using these mutants.

(12) Added quantitative analysis of biopsy and tissue model data (Mander's overlap coeJicient).

(13) Corrected and extended table 3 to take into account new primers.

(14) Added experimental details for new NMR and ITC experiments as well as new quantitative image analysis.

(15) Minor adjustments to the text to improve clarity and correct errors.

Author response:

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

Reviewer #1 (Public review):

Summary:

Bacterial species that frequently undergo horizontal gene transfer events tend to have genomes that approach linkage equilibrium, making it challenging to analyze population structure and establish the relationships between isolates. To overcome this problem, researchers have established several effective schemes for analyzing N. gonorrhoeae isolates, including MLST and NG-STAR. This report shows that Life Identification Number (LIN) Codes provide for a robust and improved discrimination between different N. gonorrhoeae isolates.

Strengths:

The description of the system is clear, the analysis is convincing, and the comparisons to other methods show the improvements offered by LIN Codes.

Weaknesses:

No major weaknesses were identified by this reviewer.

We thank the reviewer for their assessment of our paper.

Reviewer #2 (Public review):

Summary:

This paper describes a new approach for analyzing genome sequences.

Strengths:

The work was performed with great rigor and provides much greater insights than earlier classification systems.

Weaknesses:

A minor weakness is that the clinical application of LIN coding could be articulated in a more in-depth way. The LIN coding system is very impressive and is certainly superior to other protocols. My recommendation, although not necessary for this paper, is that the authors expand their analysis to noncoding sequences, especially those upstream of open reading frames. In this respect, important cis-acting regulatory mutations that might help to further distinguish strains could be identified.

We thank the reviewer for their comments. LIN code could be applied clinically, for example in the analysis of antibiotic resistant isolates, or to investigate outbreaks associated with a particular lineage. We have updated the text to note this, starting at line 432.

In regards to non-coding sequences: unfortunately, intergenic regions are generally unsuitable for use in typing systems as (i) they are subject to phase variation, which can occlude relationships based on descent; (ii) they are inherently difficult to assemble and therefore can introduce variation due to the sequencing procedure rather than biology. For the type of variant typing that LIN code represents, which aims to replicate phylogenetic clustering, protein encoding sequences are the best choice for convenience, stability, and accuracy. This is not to say that it is not a valid object to base a nomenclature on intergenic regions, which might be especially suitable for predicting some phenotypic characters, but this will still be subject to problem (ii), depending on the sequencing technology used.  Such a nomenclature system should stand beside, rather than be combined with or used in place of, phylogenetic typing. However, we could certainly investigate the relationship between an isolates LIN code and regulatory mutations in the future.

Reviewer #3 (Public review):

Summary:

In this well-written manuscript, Unitt and colleagues propose a new, hierarchical nomenclature system for the pathogen Neisseria gonorrhoeae. The proposed nomenclature addresses a longstanding problem in N. gonorrhoeae genomics, namely that the highly recombinant population complicates typing schemes based on only a few loci and that previous typing systems, even those based on the core genome, group strains at only one level of genomic divergence without a system for clustering sequence types together. In this work, the authors have revised the core genome MLST scheme for N. gonorrhoeae and devised life identification numbers (LIN) codes to describe the N. gonorrhoeae population structure.

Strengths:

The LIN codes proposed in this manuscript are congruent with previous typing methods for Neisseria gonorrhea, like cgMLST groups, Ng-STAR, and NG-MAST. Importantly, they improve upon many of these methods as the LIN codes are also congruent with the phylogeny and represent monophyletic lineages/sublineages.

The LIN code assignment has been implemented in PubMLST, allowing other researchers to assign LIN codes to new assemblies and put genomes of interest in context with global datasets.

Weaknesses:

The authors correctly highlight that cgMLST-based clusters can be fused due n to "intermediate isolates" generated through processes like horizontal gene transfer. However, the LIN codes proposed here are also based on single linkage clustering of cgMLST at multiple levels. It is unclear if future recombination or sequencing of previously unsampled diversity within N. gonorrhoeae merges together higher-level clusters, and if so, how this will impact the stability of the nomenclature.

The authors have defined higher resolution thresholds for the LIN code scheme. However, they do not investigate how these levels correspond to previously identified transmission clusters from genomic epidemiology studies. It would be useful for future users of the scheme to know the relevant LIN code thresholds for these investigations.

We thank the reviewer for their insightful comments. LIN codes do use multi-level single linkage clustering to define the cluster number of isolates. However, unlike previous applications of simple single linkage clustering such as N. gonorrhoeae core genome groups (Harrison et al., 2020), once assigned in LIN code, these cluster numbers are fixed within an unchanging barcode assigned to each isolate. Therefore, the nomenclature is stable, as the addition of new isolates cannot change previously established LIN codes.

Cluster stability was considered during the selection of allelic mismatch thresholds. By choosing thresholds based on natural breaks in population structure (Figure 3), applying clustering statistics such as the silhouette score, and by assessing where cluster stability has been maintained within the previous core genome groups nomenclature, we can have confidence that the thresholds which we have selected will form stable clusters. For example, with core genome groups there has been significant group fusion with clusters formed at a threshold of 400 allelic differences, while clustering at a threshold of 300 allelic differences has remained cohesive over time (supported by a high silhouette score) and so was selected as an important threshold in the gonococcal LIN code. LIN codes have now been applied to >27000 isolates in PubMLST, and the nomenclature has remained effective despite the continual addition of new isolates to this collection. The manuscript emphasises these points at line 96 and 346.

Work is in progress to explore what LIN code thresholds are generally associated with transmission chains. These will likely be the last 7 thresholds (25, 10, 7, 5, 3, 1, and 0 allelic differences), as previous work has suggested that isolates linked by transmission within one year are associated with <14 single nucleotide polymorphism differences (De Silva et al., 2016). The results of this analysis will be described in a future article, currently in preparation.

Harrison, O.B., et al. Neisseria gonorrhoeae Population Genomics: Use of the Gonococcal Core Genome to Improve Surveillance of Antimicrobial Resistance. The Journal of Infectious Diseases 2020.

De Silva, D., et al. Whole-genome sequencing to determine transmission of Neisseria gonorrhoeae: an observational study. The Lancet Infectious Diseases 2016;16(11):1295-1303.

Reviewer #3 (Recommendations for the authors):

(1) Data/code availability: While the genomic data and LIN codes are available in PubMLST and new isolates uploaded to PubMLST can be assigned a LIN code, it is also important to have software version numbers reported in the methods section and code/commands associated with the analysis in this manuscript (e.g. generation of core genome, statistical analysis, comparison with other typing methods) documented in a repository like GitHub.

Software version numbers have been added to the manuscript. Scripts used to run the software have been compiled and documented on protocols.io, DOI: dx.doi.org/10.17504/protocols.io.4r3l21beqg1y/v1

(2) Line 37: Missing "a" before "multi-drug resistant pathogen".

This has been corrected in the text.

(3) Line 60: Typo in geoBURST.

The text refers to a tool called goeBURST (global optimal eBURST) as described in Francisco, A.P. et al., 2009. DOI: 10.1186/1471-2105-10-152. Therefore, “geoBURST” would be incorrect.

(4) Line 136-138: It might be helpful to discuss how premature stop codons are treated in this scheme. Often in isolates with alleles containing early premature stop codons, annotation software like prokka will annotate two separate ORFs, which are then clustered with pangenome software like PIRATE. How does the cgMLST scheme proposed here treat premature stop codons? Are sequences truncated at the first stop codon, or is the nucleotide sequence for the entire gene used even if it is out of frame?

In PubMLST, alleles with premature stop codons are flagged, but otherwise annotated from the typical start to the usual stop codon, if still present. This also applies to frameshift mutations – a new unique allele will be annotated, but flagged as frameshift. In both cases, each new allele with a premature stop codon or frameshift will require human curator involvement to be assigned, to ensure rigorous allele assignment. As the Ng cgMLST v2 scheme prioritised readily auto-annotated genes, loci which are prone to internal stop codons or frameshifts with inconsistent start/end codons are excluded from the scheme. The text has been updated at line 128 to mention this.

(5) Line 213-214: What were the versions of software and parameters used for phylogenetic tree construction?

Version numbers have been added to the text between lines 214-219. Parameters have been included with the scripts documented at protocols.io DOI: dx.doi.org/10.17504/protocols.io.4r3l21beqg1y/v1

(6) Line 249: K. pneumoniae may also be a more diverse/older species than N. gonorrhoeae.

The text has been updated at line 252-253 to emphasize the difference in diversity. The age of N. gonorrhoeae as a species is a matter of scientific debate, and out of the scope of this paper to discuss.

(7) Line 278-279: Were some isolates unable to be typed, or have they just been added since the LIN code assignment occurred?

Some genomes cannot be assigned a LIN code due to poor genome quality. A minimum of 1405/1430 core genes must have an allele designated for a LIN code to be assigned. Genomes with large numbers of contigs may not meet this requirement. LIN code assignment is an ongoing process that occurs on a weekly basis in PubMLST, performed in batches starting at 23:00 (UK local time) on Sundays. The text has been updated to describe this at lines 196 and 282-283.

(8) Line 314-315: Was BAPS rerun on the dataset used in this manuscript, or is this based on previously assigned BAPS groups?

This was based on previously assigned BAPs groups, as described between lines 315-320.

(9) Line 421-423: Are there options for assigning LIN codes that do not require uploading genomes to PubMLST? I can imagine that there may be situations where researchers or public health institutions cannot share genomic data prior to publication.

Isolate data does not need to be shared to be uploaded and assigned a LIN code in PubMLST. data owners can create a private dataset within PubMLST viewable only to them, on which automated assignment will be performed. LIN code requires a central repository of genomes for new codes to be assigned in relation to. The text has been updated to emphasize this at line 197 and 427.

(10) Figure 6: How is this tree rooted? Additionally, do isolates that have unannotated LIN codes represent uncommon LIN codes or were those isolates not typed?

The tree has been left unrooted, as it is being used to visualise the relationships between the isolates rather than to explore ancestry. Detail on what LIN codes have been annotated can be found in the figure legend, which describes that the 21 most common LIN code lineages in this 1000 isolate dataset have been labelled. All 1000 isolates used in the tree had a LIN code assigned, but to ensure good legibility not all lineages were annotated on the tree. The legend has been updated to improve clarity.

Author response:

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

Reviewer #1 (Public Review):

The weaknesses of the study include the following.

(1)  It remains unclear how CDK is regulated during viral infection and how it specifically recruits E3 ligase to TBK1.

We would like to express our gratitude to the reviewer for highlighting this significant issue. The present study demonstrates that CDK2 expression is significantly upregulated upon SVCV infection in multiple fish tissues and cell lines (see Fig. 1C-F), thus suggesting that viral infection triggers CDK2 induction. However, the precise upstream signaling pathways that regulate CDK2 during viral infection remain to be fully elucidated. It is hypothesized that viral RNA sensors may activate transcription factors that bind to the cdk2 promoter; however, further investigation is required to confirm this. We have added a sentence in the Discussion (Lines 409-412) acknowledging this as a limitation and a focus for future work, suggesting potential involvement of viral sensor pathways.

With regard to the mechanism by which CDK2 recruits the E3 ligase Dtx4 to TBK1, evidence is provided that CDK2 directly interacts with both TBK1 (via its kinase domain) and Dtx4 (see Fig. 4F-I, 6A-C). Furthermore, evidence is presented demonstrating that CDK2 enhances the interaction between Dtx4 and TBK1 (Fig. 6D), thus suggesting that CDK2 functions as a scaffold protein to facilitate the formation of a ternary complex. However, further study is required to ascertain the precise structural basis of this interaction, including whether CDK2's kinase activity is required. We have added a note in the Discussion (Lines 417-421) acknowledging this limitation and proposing future structural studies to elucidate the precise binding interfaces.

(2) The implications and mechanisms for a relationship between the cell cycle and IFN production will be a fascinating topic for future studies.

We concur with the reviewer's assertion that the interplay between cell cycle progression and innate immunity constitutes a promising and under-explored research domain. Whilst the present study concentrates on the function of CDK2 in antiviral signaling, independent of its cell cycle functions, it is acknowledged that CDK2's activity is cell cycle-dependent. It is hypothesized that CDK2 may function as a molecular link between cell proliferation and immune responses, particularly in light of the observation that viral infections frequently modify host cell cycle progression. In the Discussion (lines 387-391), we now briefly propose a model wherein CDK2 activity during the S phase may suppress TBK1-mediated IFN production to allow viral replication, while CDK2 inhibition (e.g., in G1) may enhance IFN responses. This hypothesis will be the subject of our future work, including cell cycle synchronization experiments and time-course analyses of CDK2 activity and IFN output during infection.

Reviewer #1 (Recommendations for the authors):

(1) A control showing that the CDK2 inhibitor blocked kinase activity would be appropriate.

We thank the reviewer for this suggestion. We have performed experiments using the CDK2-specific inhibitor SNS-032. As shown in the Author response image 1, the treatment of EPC cells with SNS-032 (2 µM) still affect TBK1 expression. However, the selection of this inhibitor was based on literature references (ref. 1 and 2), and it is uncertain whether it directly inhibits the kinase activity of CDK2. However, our result demonstrated that CDK2 retains the capacity to degrade TBK1 even in the absence of its kinase domain (Fig. 6I), yielding outcomes that are consistent with this inhibitor.

Author response image 1.

References:

(1) Mechanism of action of SNS-032, a novel cyclin-dependent kinase inhibitor, in chronic lymphocytic leukemia. Blood. 2009 May 7;113(19):4637-45.

(2) SNS-032 is a potent and selective CDK 2, 7 and 9 inhibitor that drives target modulation in patient samples. Cancer Chemother Pharmacol. 2009 Sep;64(4):723-32.

Author response:

The following is the authors’ response to the previous reviews

Reviewers 1:

Summary:

The authors investigated the potential role of IgG N-glycosylation in Haemorrhagic Fever with Renal Syndrome (HFRS), which may offer significant insights for understanding molecular mechanisms and for the development of therapeutic strategies for this infectious disease.

While the majority of the issues have been addressed, a few minor points still remain unresolved. Quality control should be conducted prior to the analysis of clinical samples. However, the coefficient of variation (CV) value was not provided for the paired acute and convalescent-phase samples from 65 confirmed HFRS patients, which were analyzed to assess inter-individual biological variability. It is important to note that biological replication should be evaluated using general samples, such as standard serum.

We thank the reviewer for this insightful and critical comment regarding the quality control of our analytical data and the assessment of biological variability. We agree that this is essential for validating the reliability of our findings. We have now provided the requested CV data and clarified this point in the revised manuscript as detailed below.

"This dual-replicate strategy enabled a comprehensive evaluation of both biological heterogeneity and assay precision, and the coefficient of variation for samples were below 16%." Please see the Materials and Methods (Page 16, lines 360-362, and Author response table 1).

Author response table 1.

Comparative analysis of serum biomarker concentrations in acute and convalescent phase cohorts.

Reviewers 2:

This work sought to explore antibody responses in the context of hemorrhagic fever with renal syndrome (HFRS) - a severe disease caused by Hantaan virus infection. Little is known about the characteristics or functional relevance of IgG Fc glycosylation in HFRS. To address this gap, the authors analyzed samples from 65 patients with HFRS spanning the acute and convalescent phases of disease via IgG Fc glycan analysis, scRNAseq, and flow cytometry. The authors observed changes in Fc glycosylation (increased fucosylation and decreased bisection) coinciding with a 4-fold or greater increased in Haantan virus-specific antibody titer. The study also includes exploratory analyses linking IgG glycan profiles to glycosylation-related gene expression in distinct B cell subsets, using single-cell transcriptomics. Overall, this is an interesting study that combines serological profiling with transcriptomic data to shed light on humoral immune responses in an underexplored infectious disease. The integration of Fc glycosylation data with single-cell transcriptomic data is a strength.The authors have addressed the major concerns from the initial review. However, one point to emphasize is that the data are correlative. While the associations between Fc glycosylation changes and recovery are intriguing, the evidence does not establish causation. This is not a weakness, as correlative studies can still be highly valuable and informative. However, the manuscript would be strengthened by making this distinction clear, particularly in the title.

The verb "accelerated" in the title implies that the glycosylation state of IgG was a direct driver of recovery, rather than something that correlated with recovery. Thus, a more neutral word/phrase would be ideal.

We sincerely thank the reviewer for this insightful suggestion. We agree that the use of "accelerated" might overstate the potential role of IgG glycosylation, which has not been clearly clarified by our current findings. As reported in results (particularly in Figure 2), partial glycosylation exhibits statistically significant variations between seropositive and seronegative statuses, before and after seroconversion, and across different HTNV- NP specific antibody titers. Therefore, we have replaced "accelerated" with "contribute to" in the Title: "Glycosylated IgG antibodies contribute to the recovery of haemorrhagic fever with renal syndrome patients".

Author response:

Reviewer #1 (Public review):

The microbiota of Dactylorhiza traunsteineri, an endangered marsh orchid, forms complex root associations that support plant health. Using 16S rRNA sequencing, we identified dominant bacterial phyla in its rhizosphere, including Proteobacteria, Actinobacteria, and Bacteroidota. Deep shotgun metagenomics revealed high-quality MAGs with rich metabolic and biosynthetic potential. This study provides key insights into root-associated bacteria and highlights the rhizosphere as a promising source of bioactive compounds, supporting both microbial ecology research and orchid conservation.  

The manuscript presents an investigation of the bacterial communities in the rhizosphere of D. traunsteineri using advanced metagenomic approaches. The topic is relevant, and the techniques are up-to-date; however, the study has several critical weaknesses.  

We thank the reviewer for their careful reading of our manuscript and for the constructive comments. We will revise the manuscript substantially. Our responses to the specific points are below:

(1) Title: The current title is misleading. Given that fungi are the primary symbionts in orchids and were not analyzed in this study (nor were they included among other microbial groups), the use of the term "microbiome" is not appropriate. I recommend replacing it with "bacteriome" to better reflect the scope of the work.

In the revised manuscript, we will expand the Results (shotgun sequencing) and Discussion to also include fungal taxa. With these additions, the use of the term microbiome will accurately reflect the inclusion of both bacterial and fungal components.

(2) Line 124: The phrase "D. traunsteineri individuals were isolated" seems misleading. A more accurate description would be "individuals were collected", as also mentioned in line 128.

This ambiguity will be corrected in the revised manuscript.

(3) Experimental design: The major limitation of this study lies in its experimental design. The number of plant individuals and soil samples analyzed is unclear, making it difficult to assess the statistical robustness of the findings. It is also not well explained why the orchids were collected two years before the rhizosphere soil samples. Was the rhizosphere soil collected from the same site and from remnants of the previously sampled individuals in 2018? This temporal gap raises serious concerns about the validity of the biological associations being inferred.

In the revised manuscript, we will explicitly state the number of individuals and soil samples included in the study, and we will more clearly describe the sequence of sampling events. We will also add a dedicated statement in the Discussion addressing the temporal gap between plant sampling and rhizosphere soil collection, acknowledging that this is a limitation of the study.

(4) Low sample size: In lines 249-251 (Results section), the authors mention that only one plant individual was used for identifying rhizosphere bacteria. This is insufficient to produce scientifically robust or generalizable conclusions.

In the revised manuscript, we will clearly state that only one rhizosphere sample was available and will frame the study as exploratory in nature. We will explicitly acknowledge this limitation in both the Methods and Discussion, and we will temper our conclusions accordingly.

(5) Contextual limitations: Numerous studies have shown that plant-microbe interactions are influenced by external biotic and abiotic factors, as well as by plant age and population structure. These elements are not discussed or controlled for in the manuscript. Furthermore, the ecological and environmental conditions of the site where the plants and soil were collected are poorly described. The number of biological and technical replicates is also not clearly stated.

In the revised manuscript, we will expand the description of the collection site and environmental conditions to the extent supported by our records. We will also clearly state the number of biological and technical replicates used for each analysis. In the Discussion, we will explicitly acknowledge that plant age, environmental variables, and other biotic/abiotic factors may influence plant–microbe interactions and were not directly assessed in this study.

(6) Terminology: Throughout the manuscript, the authors refer to the "microbiome," though only bacterial communities were analyzed. This terminology is inaccurate and should be corrected consistently.

As noted in our response to point (1), we will revise terminology throughout the manuscript to ensure consistency and to accurately reflect the expanded bacterial and fungal coverage in the revised version.

Reviewer #2 (Public review):

The authors aim to provide an overview of the D. traunsteineri rhizosphere microbiome on a taxonomic and functional level, through 16S rRNA amplicon analysis and shotgun metagenome analysis. The amplicon sequencing shows that the major phyla present in the microbiome belong to phyla with members previously found to be enriched in rhizospheres and bulk soils. Their shotgun metagenome analysis focused on producing metagenome assembled genomes (MAGs), of which one satisfies the MIMAG quality criteria for high-quality MAGs and three those for medium-quality MAGs. These MAGs were subjected to functional annotations focusing on metabolic pathway enrichment and secondary metabolic pathway biosynthetic gene cluster analysis. They find 1741 BGCs of various categories in the MAGs that were analyzed, with the high-quality MAG being claimed to contain 181 SM BGCs. The authors provide a useful, albeit superficial, overview of the taxonomic composition of the microbiome, and their dataset can be used for further analysis.

The conclusions of this paper are not well-supported by the data, as the paper only superficially discusses the results, and the functional interpretation based on taxonomic evidence or generic functional annotations does not allow drawing any conclusions on the functional roles of the orchid microbiota.  

We thank the reviewer for their thoughtful and constructive assessment of our manuscript. The comments have been very helpful in identifying areas where the clarity, structure, and interpretation of our work can be improved. Our responses to the specific points are below:

(1) The authors only used one individual plant to take samples. This makes it hard to generalize about the natural orchid microbiome.

We agree with the reviewer that the limited number of plant individuals restricts the generality of the conclusions. In the revised manuscript, we will clearly state that only one rhizosphere sample was available for analysis and will frame the study as exploratory. We will also explicitly acknowledge this limitation in the Discussion and ensure that our interpretations and conclusions remain appropriately cautious.

(2) The authors use both 16S amplicon sequencing and shotgun metagenomics to analyse the microbiome. However, the authors barely discuss the similarities and differences between the results of these two methods, even though comparing these results may be able to provide further insights into the conclusions of the authors. For example, the relative abundance of the ASVs from the amplicon analysis is not linked to the relative abundances of the MAGs.

In the revised manuscript, we will expand the Results and Discussion to include a clearer comparison between the taxonomic profiles derived from 16S amplicon sequencing and those obtained from shotgun metagenomic binning.

(3) Furthermore, the authors discuss that phyla present in the orchid microbiome are also found in other microbiomes and are linked to important ecological functions. However, their results reach further than the phylum level, and a discussion of genera or even species is lacking. The phyla that were found have very large within-phylum functional variability, and reliable functional conclusions cannot be drawn based on taxonomic assignment at this level, or even the genus level (Yan et al. 2017).

In the revised manuscript, we will incorporate taxonomic discussion at finer resolution where reliable assignments are available. We will also revise the Discussion to avoid overinterpreting phylum-level taxonomy in terms of ecological function.

(4) Additionally, although the authors mention their techniques used, their method section is sometimes not clear about how samples or replicates were defined. There are also inconsistencies between the methods and the results section, for example, regarding the prediction of secondary metabolite biosynthetic gene clusters (BGCs).

In the revised Methods section, we will clearly define the number and type of samples included in each analysis, specify the number of replicates and how they were handled, and provide a clearer description of the biosynthetic gene cluster (BGC) prediction workflow, including the tools used and how results were interpreted. 

(5) The BGC prediction was done with several tools, and the unusually high number of found BGCs (181 in their high-quality MAG) is likely due to false positives or fragmented BGCs. The numbers are much higher than any numbers ever reported in literature supported by functional evidence (Amos et al, 2017), even in a prolific genus like Streptomyces (Belknap et al., 2020). This caveat is not discussed by the authors.

We thank the reviewer for this important point. Our original intention was to present the BGC predictions as a resource for future exploration, which is why multiple tools were used. However, we understand how this approach may lead to confusion, particularly regarding the confidence level of the predicted clusters and the potential inflation of counts due to assembly fragmentation or tool sensitivity. In the revised manuscript, we will thoroughly revise this section to clearly distinguish highconfidence predictions from more exploratory findings. We will focus on results supported by stronger evidence, explicitly qualify lower-confidence predictions as putative, and temper any functional interpretations accordingly.

(6) The authors have generated one high-quality MAG and three medium-quality MAGs. In the discussion, they present all four of these as high-quality, which could be misleading. The authors discuss what was found in the literature about the role of the bacterial genera/phyla linked to these MAGs in plant rhizospheres, but they do not sufficiently link their own analysis results (metabolic pathway enrichment and biosynthetic gene cluster prediction) to this discussion. The results of these analyses are only presented in tables without further explanation in either the results section or the discussion, even though there may be interesting findings. For example, the authors only discuss the class of the BGCs that were found, but don't search for experimentally verified homologs in databases, which could shed more light on the possible functional roles of BGCs in this microbiome.

In the revised manuscript, we will ensure that MAG quality is described accurately and consistently throughout, distinguishing clearly between high-quality and medium-quality bins according to accepted standards.

(7) In the conclusions, the authors state: "These analyses uncovered potential metabolic capabilities and biosynthetic potentials that are integral to the rhizosphere's ecological dynamics." I don't see any support for this. Mentioning that certain classes of BGCs are present is not enough to make this claim, in my opinion. Any BGC is likely important for the ecological niche the bacteria live in. The fact that rhizosphere bacteria harbour BGCs is not surprising, and it doesn't tell us more than is already known.

In the revised manuscript, we will rewrite the conclusion to reflect a more cautious interpretation, focusing on the potential metabolic and biosynthetic capabilities suggested by the data without asserting ecological roles that cannot be directly supported. These capabilities will be presented as hypotheses for future investigation rather than established ecological features.

Author response:

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

Reviewer #1 (Public review):

The authors used fluorescence microscopy, image analysis, and mathematical modeling to study the effects of membrane affinity and diffusion rates of MinD monomer and dimer states on MinD gradient formation in B. subtilis. To test these effects, the authors experimentally examined MinD mutants that lock the protein in specific states, including Apo monomer (K16A), ATP-bound monomer (G12V), and ATPbound dimer (D40A, hydrolysis defective), and compared to wild-type MinD. Overall, the experimental results support the conclusion that reversible membrane binding of MinD is critical for the formation of the MinD gradient, but that the binding affinities between monomers and dimers are similar.  

The modeling part is a new attempt to use the Monte Carlo method to test the conditions for the formation of the MinD gradient in B. subtilis. The modeling results provide good support for the observations and find that the MinD gradient is sensitive to different diffusion rates between monomers and dimers. This simulation is based on several assumptions and predictions, which raises new questions that need to be addressed experimentally in the future. However, the current story is sufficient without testing these assumptions or predictions.

Reviewer #2 (Public review): 

Summary:  

Bohorquez et al. investigate the molecular determinants of intracellular gradient formation in the B. subtilis Min system. To this end, they generate B. subtilis strains that express MinD mutants that are locked in the monomeric or dimeric states, and also MinD mutants with amphipathic helices of varying membrane affinity. They then assess the mutants' ability to bind to the membrane and form gradients using fluorescence microscopy in different genetic backgrounds. They find that, unlike in the E. coli Min system, the monomeric form of MinD is already capable of membrane binding. They also show that MinJ is not required for MinD membrane binding and only interacts with the dimeric form of MinD. Using kinetic

Monte Carlo simulations, the authors then test different models for gradient formation, and find that a MinD gradient along the cell axis is only formed when the polarly localized protein MinJ stimulates dimerization of MinD, and when the diffusion rate of monomeric and dimeric MinD differs. They also show that differences in the membrane affinity of MinD monomers and dimers are not required for gradient formation.  

Strengths:  

The paper offers a comprehensive collection of the subcellular localization and gradient formation of various MinD mutants in different genetic backgrounds. In particular, the comparison of the localization of these mutants in a delta MinC and MinJ background offers valuable additional insights. For example, they find that only dimeric MinD can interact with MinJ. They also provide evidence that MinD locked in a dimer state may co-polymerize with MinC, resulting in a speckled appearance.  

The authors introduce and verify a useful measure of membrane affinity in vivo.  

The modulation of the membrane affinity by using distinct amphipathic helices highlights the robustness of the B. subtilis MinD system, which can form gradients even when the membrane affinity of MinD is increased or decreased.  

Weaknesses:  

The main claim of the paper, that differences in the membrane affinity between MinD monomers and dimers are not required for gradient formation, does not seem to be supported by the data. The only measure of membrane affinity presented is extracted from the transverse fluorescence intensity profile of cells expressing the mGFP-tagged MinD mutants. The authors measure the valley-to-peak ratio of the profile, which is lower than 1 for proteins binding to the membrane and higher than 1 for cytosolic proteins. To verify this measure of membrane affinity, they use a membrane dye and a soluble GFP, which results in values of ~0.75 and ~1.25, respectively. They then show that all MinD mutants have a value - roughly in the range of 0.8-0.9 - and they use this to claim that there are no differences in membrane affinity between monomeric and dimeric versions.  

While this way to measure membrane affinity is useful to distinguish between binders and non-binders, it is unclear how sensitive this assay is, and whether it can resolve more subtle differences in membrane affinity, beyond the classification into binders and non-binders. A dimer with two amphipathic helices should have a higher membrane affinity than a monomer with only one such copy. Thus, the data does not seem to support the claim that "the different monomeric mutants have the same membrane affinity as the wildtype MinD". The data only supports the claim that B. subtilis MinD monomers already have a measurable membrane affinity, which is indeed a difference from the E. coli Min system.  

While their data does show that a stark difference between monomer and dimer membrane affinity may not be required for gradient formation in the B. subtilis case, it is also not prevented if the monomer is unable to bind to the membrane. They show this by replacing the native MinD amphipathic helix with the weak amphipathic helix NS4AB-AH. According to their membrane affinity assay, NS4AB-AH does not bind to the membrane as a monomer (Figure 4D), but when this helix is fused to MinD, MinD is still capable of forming a gradient (albeit a weaker one). Since the authors make a direct comparison to the E. coli MinDE systems, they could have used the E. coli MinD MTS instead or in addition to the NS4AB-AH amphipathic helix. The reviewer suspects that a fusion of the E. coli MinD MTS to B. subtilis MinD may also support gradient formation.  

The paper contains insufficient data to support the many claims about cell filamentation and minicell formation. In many cases, statements like "did not result in cell filamentation" or "restored cell division" are only supported by a single fluorescence image instead of a quantitative analysis of cell length distribution and minicell frequency, as the one reported for a subset of the data in Figure 5.  

The paper would also benefit from a quantitative measure of gradient formation of the distinct MinD mutants, instead of relying on individual fluorescent intensity profiles.  

The authors compare their experimental results with the oscillating E. coli MinDE system and use it to define some of the rules of their Monte Carlo simulation. However, the description of the E. coli Min system is sometimes misleading or based on outdated findings.

The Monte Carlo simulation of the gradient formation in B. subtilis could benefit from a more comprehensive approach:

(1) While most of the initial rules underlying the simulation are well justified, the authors do not implement or test two key conditions:

(a) Cooperative membrane binding, which is a key component of mathematical models for the oscillating E. coli Min system. This cooperative membrane binding has recently been attributed to MinD or MinCD oligomerization on the membrane and has been experimentally observed in various instances; in fact, the authors themselves show data supporting the formation of MinCD copolymers.  

(2) Local stimulation of the ATPase activity of MinD which triggers the dimer-to-monomer transition; E. coli MinD ATP hydrolysis is stimulated by the membrane and by MinE, so B. subtilis MinD may also be stimulated by the membrane and/or other components like MinJ. Instead, the authors claim that (a) would only increase differences in diffusion between the monomer and different oligomeric species, and that a 2-fold increase in dimerization on the membrane could not induce gradient formation in their simulation, in the absence of MinJ stimulating gradient formation. However, a 2-fold increase in dimerization is likely way too low to explain any cooperative membrane binding observed for the E. coli Min system. Regarding (b), they also claim that implementing stimulation of ATP hydrolysis on the membrane (dimer-to-monomer transition) would not change the outcome, but no simulation result for this condition is actually shown.  

(3) To generate any gradient formation, the authors claim that they would need to implement stimulation of dimer formation by MinJ, but they themselves acknowledge the lack of any experimental evidence for this assertion. They then test all other conditions (e.g., differences in membrane affinity, diffusion, etc.) in addition to the requirement that MinJ stimulates dimer formation. It is unclear whether the authors tested all other conditions independently of the "MinJ induces dimerization" condition, and whether either of those alone or in combination could also lead to gradient formation. This would be an important test to establish the validity of their claims.

Reviewer #3 (Public review): 

This important study by Bohorquez et al examines the determinants necessary for concentrating the spatial modulator of cell division, MinD, at the future site of division and the cell poles. Proper localization of MinD is necessary to bring the division inhibitor, MinC, in proximity to the cell membrane and cell poles where it prevents aberrant assembly of the division machinery. In contrast to E. coli, in which MinD oscillates from pole to pole courtesy of a third protein MinE, how MinD localization is achieved in B. subtilis - which does not encode a MinE analog - has remained largely a mystery. The authors present compelling data indicating that MinD dimerization is dispensable for membrane localization but required for concentration at the cell poles. Dimerization is also important for interactions between MinD and MinC, leading to the formation of large protein complexes. Computational modeling, specifically a Monte Carlo simulation, supports a model in which differences in diffusion rates between MinD monomers and dimers lead to the concentration of MinD at cell poles. Once there, interaction with MinC increases the size of the complex, further reinforcing diffusion differences. Notably, interactions with MinJ-which has previously been implicated in MinCD localization, are dispensable for concentrating MinD at cell poles although MinJ may help stabilize the MinCD complex at those locations.  

Reviewer #1 (Recommendations for the authors):  

(1) The title could be modified to better reflect the emphasis on MinD monomer and dimer diffusion rather than the fact that membrane affinity is not important in MinD gradient formation. In addition, because membrane association requires affinity for the membrane, this title seems inconsistent with statements in the main text, such as Lines 246-247: a reversible membrane association is important for the formation of a MinD gradient along the cell axis.

We agree with the reviewer that the title can be more accurate, and we have now changed it to “Membrane affinity difference between MinD monomer and dimer is not crucial to MinD gradient formation in Bacillus subtilis”

(2) This paper reports that the difference in diffusion rates between MinD monomers and dimers is an important factor in the formation of Bs MinD gradients. However, one can argue for the importance of MinD monomers in the cellular context. Since the abundance of ATP in cells often far exceeds the abundance of MinD protein molecules under experimental conditions, MinD can easily form dimers in the cytoplasm. How does the author address this problem?  

It is a good point that ATP concentration in the cell likely favours dimers in the cytoplasm. However, what is important in our model is that there is cycling between monomer and dimer, rather than where exactly this happen. In fact, the gradients works essentially equally well if dimers can become monomers only whilst they are at the membrane, as we have mentioned in the manuscript (lines 324-326 in the original manuscript). However, in the original manuscript this simulation was not shown, and now we have included this in the new Fig. 8D & E.

(3)The claim "This oscillating gradient requires cycling of MinD between a monomeric cytosolic and a dimeric membrane attached state." (Lines 46, 47) is not well supported by most current studies and needs to be revised since to my knowledge, most proposed models do not consider the monomer state. The basic reaction steps of Ec Min oscillations include ATP-bound MinD dimers attaching to the membrane that subsequently recruit more MinD dimers and MinE dimers to the membrane; MinE interactions stimulate ATP hydrolysis in MinD, leading to dissociation of ADP-bound MinD dimers from the membrane; nucleotide exchange occurs in the cytoplasm.  

Here the reviewer refers to a sentence in a short “Importance” abstract that we have added. In fact, such abstract is not necessary, so we have removed it. Of note, the E. coli MinD oscillation, including the role of MinE, is described in detail in the Introduction. 

A recent reference is a paper by Heermann et al. (2020; doi: 10.1016/j.jmb.2020.03.012), which considers the MinD monomer state, which is not mentioned in this work. How do their observations compare to this work?  

The Heermann paper mentions that MinD bound to the membrane displays an interface for multimerization, and that this contributes to the local self-enhancement of MinD at the membrane. In our Discussion, we do mention that E. coli MinD can form polymers in vitro and that any multimerization of MinD dimers will further increase the diffusion difference between monomer and dimer, and might contribute to the formation of a protein gradient (lines 459-467). We have now included a reference to the Heermann paper (line 461).

(4) Throughout the manuscript, errors in citing references were found in several places.                 

We have corrected this where suggested.

(5) The introduction may be somewhat misleading due to mixed information from experimental cellular results, in vitro reconstructions, and theoretical models in cells or in vitro environments. Some models consider space constraints, while others do not. Modifications are recommended to clarify differences.  

See below for responses 

(6) The citation for MinD monomers:

The paper by Hu and Lutkenhaus (2003, doi: 10.1046/j.1365-2958.2003.03321.x.) contains experimental evidence showing monomer-dimer transition using purified proteins. Another paper by the same laboratory (Park et al. 2012, doi: 10.1111/j.1365-2958.2012.08110.x.) explained how ATP-induced dimerization, but this paper is not cited.  

The Park et al. 2012 paper focusses at the asymmetric activation of MinD ATPase by MinE, which goes beyond the scope of our work. However, we have cited several other papers from the Lutkenhaus lab, including the Wu et al. 2011 paper describing the structure of the MinD-ATP complex.

Other evidence comes from structural studies of Archaea Pyrococcus furiosus (1G3R) and Pyrococcus horikoshii (1ION), and thermophilic Aquifex aeolicus (4V01, 4V02, 4V03). As they may function differently from Ec MinD, they are less relevant to this manuscript.

We agree. 

(7) Lines 65, 66: Using the term 'a reaction-diffusion couple' to describe the biochemical facts by citing references of Hu and Lutkenhaus (1999) and Raskin and de Boer (1999) is not appropriate. The idea that the Min system behaves as a reaction-diffusion system was started by Howard et al. (2001), Meinhardt and de Boer (2001), and Huang et al. (2003) et al. In addition, references for MinE oscillation are missing. 

We have now corrected this (line 52).

(8) Lines 77-79: Citations are incorrect.

ATP-induced dimerization: Hu and Lutkenhaus (2003, DOI: 10.1046/j.1365-2958.2003.03321.x), Park et al. (2012). C-terminal amphipathic helix formation: Szeto et al. (2003), Hu and Lutkenhaus (2003, DOI: 10.1046/j.1365-2958.2003.03321.x).

Citations have been corrected.

(9) Line 78: The C-terminal amphipathic helix is not pre-formed and then exposed upon conformational change induced by ATP-binding. This alpha-helical structure is an induced fold upon interaction with membranes as experimentally demonstrated by Szeto et al. (2003).  

We have adjusted the text to correct this (lines 64-66).

(10) Line 102: 'cycles between membrane association and dissociation of MinD' also requires MinE in addition to ATP.

We believe that in the context of this sentence and following paragraph it is not necessary to again mention MinE, since it is focused on parallels between the E. coli and B. subtilis MinD membrane binding cycles.

(11) In the introduction, could the author briefly explain to a general audience the difference between Monte Carlo and reaction-diffusion methods? How do different algorithms affect the results?

The main difference between the kinetic Monte Carlo and typical reaction-diffusion methods which is relevant to our work is that the first is particle-based, and naturally includes statistical fluctuations (noise), whereas the second is field-based, and is in the normal implementation deterministic, so does not include noise. Whilst it should be noted that one can in principle include noise in the field-based reactiondiffusion methods, this is done rarely. Additionally, although we do not do this here, the kinetic MonteCarlo can also account, in principle, for particle shape (sphere versus rod), or for localized interactions (as sticky patches on the surface): therefore the kinetic Monte Carlo is more microscopic in nature. We have now shortly described the difference in lines 102-105.

(12)  Lines 126-128: The second part of the sentence uses the protein structure of Pyrococcus furiosus MinD (Ref 37) to support a protein sequence comparison between Ec and Bs MinD. However, the structure of the dimeric E. coli MinD-ATP complex (3Q9L) is available, which is Reference 38 that is more suited for direct comparison.

To discuss monomeric MinD from P. furiosus, it will be useful to include it in the primary sequence alignment in Figure S1.

We do not think that this detailed information is necessary to add to Figure S1, since the mutants have been described before (appropriate citations present in the text).

(13) Lines 127, 166: Where Figure S1 is discussed, a structural model of MinD will be useful alongside with the primary sequence alignment.

We do not think that this detailed information is necessary to understand the experiments since the mutants have been described before.

(14) Lines 131-132: Reference is missing for the sentence of " the conserved..."; Reference 38.  In Reference 38, there is no experimental evidence on G12 but inferred from structure analysis. Reference 26 discusses ATP and MinE regulation on the interactions between MinD and phospholipid bilyers; not about MinD dimerization.

We have corrected this and added the proper references. 

For easy reading, the mutant MinD phenotypes can be indicated here instead of in the figure legends, including K16A (apo monomer), MinD G12V (ATP-bound monomer), and MinD D40A (ATP-bound dimer, ATP hydrolysis deficient).  

We have added the suggested descriptions of the mutants in the main text.

(15) Lines 150-151: Unlike Ec MinD, which forms a clear gradient in one half of the cell, Bs MinD (wild type) mainly accumulates at the hemispheric poles. What percentage of a cell (or cell length) can be covered by the Bs MinD gradient? How does the shaded area in the longitudinal FIP compare to the area of the bacterial hemispherical pole? If possible, it might be interesting to compare with the range of nucleoid occlusion mechanisms that occur.

Part of the MinD gradient covers the nucleoid area, since the fluorescence signal is still visible along the cell lengths, yet there is no sudden drop in fluorescence, suggesting that nucleoid exclusion does not play a role.

(16)  Line 160: In addition to summarizing the membrane-binding affinity, descriptions of the differences in the gradient distribution or formation will be useful.  

We have done this in lines 155-156 of the original manuscript: “The monomeric ATP binding G12V variant shows the same absence of a protein gradient as the K16A variant”.

(17) Line 262: 'distribution' is not shown.  

We do not understand this remark. This information is shown in Fig. 5B (now Fig. 6B).

(18)  Line 287: Wrong citation for reference 31.

Reference has been corrected.

(19)  Line 288 and lines 596 regarding the Monte Carlo simulation:

(a)  An illustration showing the reaction steps for MinD gradient formation will help understand the rationale and assumptions behind this simulation.

We have added an illustration depicting the different modelling steps in the new Fig. 8.

(b)  Equations are missing.

(c)   A table summarizing the parameters used in the simulation and their values.

(d)  For general readers, it will be helpful to convert the simulation units to real units.

(e)  Indicate real experimental data with a citation or the reason for any speculative value.

The Methods section provides a discussion of all parameters used in the potentials on which our kinetic Monte-Carlo algorithm is based. We have now also provided a Table in the SI (Table S1) with typical parameter values in both simulation units and real units. The experimental data and reasoning behind the values chosen are discussed in the Methods section (see “Kinetic Monte Carlo simulation”).

(20)  Lines 320-321: Reference missing.

The interaction between MinJ and the dimer form of MinD is based on our findings shown in the original Fig. S4, and this information has not been published before. We have rephrased the sentence to make it more clear. Of note, Fig. S4 has been moved to the main manuscript, at the request of reviewer #2, and is now new Fig. 2. 

(21)  Lines 355-359: Is the statement specifically made for the Bs Min system? Is there any reference for the statement? Isn't the differences in diffusion rates between molecules 'at different locations' in the system more important than reducing their diffusion rates alone? It is unclear about the meaning of the statement "the Min system uses attachment to the membrane to slow down diffusion". Is this an assumption in the simulation?

The statement is generic, however the reviewer has a good point and we have made this statement more clear by changing “considerably reduced diffusion rate” to “locally reduced diffusion rate” (line 359).

(22) Line 403: Citation format.

We have corrected the text and citation.

(23) Lines 442-444: The parameters are not defined anywhere in the manuscript.

Discussed in the M&M and in the new Table S1.

(24) Lines 464-465: Regarding the final sentence, what does 'this prediction' refer to? Hasn't the author started with experimental observations, predicted possible factors of membrane affinity and diffusion rates, and used the simulation approach to disapprove or support the prediction?

We have changed “prediction” to “suggestion”, to make it clear that it is related to the suggestion in the previous sentence that  “our modelling suggests that stimulation of MinD-dimerization at cell poles and cell division sites is needed.” (line 471).

(25) Materials and Methods: Statistical methods for data analyses are missing.

Added to “Microscopy” section.

(26) References: References 34, 40, 51 are incomplete.

References 34 and 40 have been corrected. Reference 51 is a book.

(27)  Figures: The legends (Figures 1-7) can be shortened by removing redundant details in Material and Methods. Make sure statistical information is provided. The specific mutant MinD states, including Apo monomer, ATP-bound dimer, ATP hydrolysis deficient, and non-membrane binding etc can be specified in the main text. They are repeated in the legends of Figures 1 and 2.

We have removed redundant details from the legends and provided statistical information.

(28)  Supporting information:

Table S1: Content of the acknowledgment statement may be moved to materials and methods and the acknowledgment section. Make sure statistical information is provided in the supporting figure legends.

We are not sure what the reviewer means with the content acknowledgement in Table S1 (now Table S2). Statistical information has been added.

Figure S1. Adding a MinD structure model will be useful.

We do not think that a structural model will enlighten our results since our work is not focused at structural mutagenesis. The mutants that we use have been described in other papers that we have cited.

Reviewer #2 (Recommendations for the authors):  

The authors should cite and relate their data to the preprint by Feddersen & Bramkamp, BioRxiv 2024. ATPase activity of B. subtilis MinD is activated solely by membrane binding.

We have now discussed this paper in relation to our data in lines 407-409. 

I am not convinced the authors are able to make the statement in lines 160-161 based on their assay: "This confirmed that the different monomeric mutants have the same membrane affinity as wild-type MinD". It is unclear if measuring valley-to-peak ratios in their longitudinal profiles can resolve small differences in membrane affinity. Wildtype MinD should at least be dimeric, or (as the authors also note elsewhere) may even be present in higher-order structures and as such have a higher membrane affinity than a monomeric MinD mutant. The authors should rephrase the corresponding sections in the manuscript to state that the MinD monomer already has detectable membrane affinity, instead of stating that the monomer and dimer membrane affinity are the same.

We agree that “the same affinity” is too strongly worded, and we have now rephrased this by saying that the different monomeric mutants have a comparable membrane affinity as wild type MinD (line 152).

According to the authors' analysis, MinD-NS4B would not bind to the membrane as it has a valley-to-peak ratio higher than 1, similar to the soluble GFP. However, the protein is clearly forming a gradient, and as such probably binding to the membrane. The authors should discuss this as a limitation of their membrane binding measure.

The ratio value of 1 is not a cutoff for membrane binding. As shown in Fig. 1F, GFP has a valley-topeak ratio close to 1.25, whereas the FM5-95 membrane dye has a ratio close to 0.75. In Fig. 3C (now Fig. 4C) we have shown that GFP fused with the NS4B membrane anchor has a lower ratio than free GFP, and we have shown the same in Fig. 4D (now Fig. 5D) for GFP-MinD-NS4B. The difference are small but clear, and not similar to GFP.

The observation that MinD dimers are localized by MinJ is interesting and key to the rule of the Monte Carlo simulation that dimers attach to MinJ. However, the data is hidden in the supplementary information and is not analysed as comprehensively, e.g., it lacks the analysis of the membrane binding. The paper would benefit from moving the fluorescence images and accompanying analysis into the main text.  

We have moved this figure to the main text and added an analysis of the fluorescence intensities (new Fig. 2).

The authors should show the data for cell length and minicell formation, not only for the MinDamphipathic helix versions (Fig. 5), but also for the GFP-MinD, and all the MinD mutants. They do refer to some of this data in lines 145-148 but do not show it anywhere. They also refer to "did not result in cell filamentation" in line 213 and to "resulted in highly filamentous cells" and "Introduction of a minC deletion restored cell division" in lines 167-160 without showing the cell length and minicell data, but instead refer to the fluorescence image of the respective strain. I would suggest the authors include this data either in a subpanel in the respective figure or in the supplementary information.

The effect of uncontrolled MinC activity is very apparent and leads to long filamentous cells. Also the occurrence of minicells is apparent. Cell lengths distribution of wild type cells is shown in Fig. 6B, and minicell formation is negligibly small in wild type cells.

The transverse fluorescence intensity profiles used as a measure for membrane binding are an average profile from ~30 cells. In the case of the longitudinal profiles that display the gradient, only individual profiles are displayed. I understand that because of distinct cell length, the longitudinal profiles cannot simply be averaged. However, it is possible to project the profiles onto a unit length for averaging (see for example the projection of profiles in McNamara. et al., BioRxiv (2023)). It would be more convincing to average these profiles, which would allow the authors to also quantify the gradients in more detail. If that is impossible, the authors may at least quantify individual valley-to-peak ratios of the longitudinal fluorescence profiles as a measure of the gradient.

We agree that in future work it would be better to average the profiles as suggested. However, due to limited time and resources, we cannot do this for the current manuscript.

Regarding the rules and parameters used for the Monte Carlo simulation (see also the corresponding sections in the public review):

(1) The authors mention that they have not included multimerization of MinD in their simulation but argue in the discussion that it would only strengthen the differences in the diffusion between monomers and multimers. This is correct, but it may also change the membrane residence time and membrane affinity drastically.

Simulation of multimerization is difficult, but we have now included a simulation whereby MinD dimers can also form tetramers (lines 341-348), shown in the new Fig. 8K. This did not alter the MinD gradient much. 

(2) The authors implement a dimer-to-monomer transition rate that they equate with the stochastic ATP hydrolysis rate occurring with a half-life of approximately 1/s (line 305). They claim that this rate is based on information from E. coli and cite Huang and Wingreen. However, the Huang paper only mentions the nucleotide exchange rate from ADP to ATP at 1/s. Later that paper cites their use of an ATP hydrolysis rate of 0.7/s to match the E. coli MinDE oscillation rate of 40s. From the authors' statement, it is unclear to me whether they refer to the actual ATP hydrolysis rate in Huang and Wingreen or something else. For E. coli MinD, both the membrane and MinE stimulate ATPase activity. Even if B. subtilis lacks MinE, ATP hydrolysis may still be stimulated by the membrane, which has also been reported in another preprint (Feddersen & Bramkamp, BioRxiv 2024). It may also be stimulated by other components of the Min system like MinJ. The authors should include in the manuscript the Monte Carlo simulation implementing dimer to monomer transition on the membrane only, which is currently referred to only as "(data not shown)". 

The exact value of the ATP hydrolysis rate is not so important here, so 1/s only gives the order of magnitude (in line with 0.7/s above), which we have now clarified in lines 631-632. We have now also added the “(data not shown” results to Fig. 8, i.e. simulations where dimer to monomer transitions (i.e. ATPase activity) only occurs at the membrane (Fig. 8D & E, and lines 319-322).

(3) How long did the authors simulate for? How many steps? What timesteps does the average pictured in Figure 7 correspond to?

We simulated 10^7time steps (corresponding to 100 s in real time). We have checked that the simulation steps for which we average are in steady state. Typical snapshots are recorded after 10^610^7time steps, when the system is in steady state. We have added this information in lines 299-300.

There are several misconceptions about the (oscillating E. coli) Min system in the main text:

(1) Lines 77-78: "In case of the E. coli MinD, ATP binding leads to dimerization of MinD, which induces a conformational change in the C-terminal region, thereby exposing an amphiathic helix that functions as a membrane binding domain" and "This shows a clear difference with the E. coli situation, where dimerization of MinD causes a conformational change of the C-terminal region enabling the amphipathic helix to insert into the lipid bilayer" in lines 400-403 are incorrect. There is no evidence that the amphipathic helix at the C-terminus of MinD changes conformation upon ATP binding; several studies have shown instead that a single copy of the amphipathic helix is too weak to confer efficient membrane binding but that the dimerization confers increased membrane binding as now two amphipathic helices are present leading to an avidity effect in membrane binding. Please refer to the following papers (Szeto et al., JBC (2003); Wu et al., Mol Microbiol (2011); Park et al., Cell (2011); Heermann et al., JMB (2020); Loose et al., Nat Struct Mol Biol (2011); Kretschmer et al., ACS Syn Biol (2021); Ramm et al., Nat Commun (2018) or for a better overview the following reviews on the topic of the E. coli Min system Wettmann and Kruse, Philos Trans R Soc B Biol (2018), Ramm et al., Cell and Mol Life Sci (2019); Halatek et al., Philos Trans R SocB Biol Sci (2018).

This is indeed incorrectly formulated, and we have now amended this in lines 64-66 and lines 403406. Key papers are cited in the text.

(2) The authors mention that E. coli MinD may multimerize, citing a study where purified MinD was found to polymerize, and then suggest that this is unlikely to be the case in B. subtilis as FRAP recovery of MinD is quick. However, cooperativity in membrane binding is essential to the mathematical models reproducing E. coli Min oscillations, and there is more recent experimental evidence that E. coli MinD forms smaller oligomers that differ in their membrane residence time and diffusion (e.g., Heermann et al., Nat Methods (2023); Heermann et al., JMB (2020);) I would suggest the authors revise the corresponding text sections and test the multimerization in their simulation (see above).

As mentioned above, simulating oligomerization is difficult, but in order to approximate related cooperative effects, we have simulated a situation whereby MinD dimers can form tetramers. This simulation did not show a large change in MinD gradient formation. We have added the result of this simulation to Fig. 8 (Fig. 8K), and discuss this further in lines 341-348 and 459-467.

(3) Lines 75-76 and lines 79-80: The sentences "MinC ... and needs to bind to the Walker A-type ATPase MinD for its activity" and "The MinD dimer recruits MinC ... and stimulates its activity" are misleading. MinC is localized by MinD, but MinD does not alter MinC activity, as MinC mislocalization or overexpression also prevents FtsZ ring formation leading to minicell or filamentous cells, as also later described by the authors (line 98). There is also no biochemical evidence that the presence of MinD somehow alters MinC activity towards FtsZ other than a local enrichment on the membrane. I would rephrase the sentence to emphasize that MinD is only localizing MinC but does not alter its activity.   

We have rephrased this sentence to prevent misinterpretation (lines 66-67).

Minor points:  

(1)  I am not quite sure what the experiment with the CCCP shows. The authors explain that MinD binding via the amphipathic helix requires the presence of membrane potential and that the addition of CCCP disturbs binding. They then show that the MinD with two amphipathic helices is not affected by CCCP but the wildtype MinD is. What is the conclusion of this experiment? Would that mean that the MinD with two amphipathic helices binds more strongly, very differently, perhaps non-physiologically?  

This experiment was “To confirm that the tandem amphipathic helix increased the membrane affinity of MinD”, as mentioned in the beginning of the paragraph (line 224).  

(2) Lines 456-457: Please cite the FRAP experiment that shows a quick recovery rate of MinD.

Reference has been added. 

(3) Figure 4D: It is unclear to me to which condition the p-value brackets point.

This is related to a statistical t-test. We have added this information to the legend of the figure.

(4) Line 111, "in the membrane affinity of the MinD". I think that the "the" before MinD should be removed.  

Corrected

(5) Typo in line 199 "indicting" instead of indicating.

Corrected

(6) Typo in line 220 "reversable" instead of reversible.

Corrected

(7) Lines 279, 284, 905: "Monte-Carlo" should read Monte Carlo.

Corrected

Reviewer #3 (Recommendations for the authors):  

Introduction: As written, the introduction does not provide sufficient background for the uninitiated reader to understand the function of the MinCD complex in the context of assembly and activation of cell division in B. subtilis. The introduction is also quite long and would benefit from condensing the description of the Min oscillation mechanism in E. coli to one or two sentences. While highlighting the role of MinE in this system is important for understanding how it works, it is only needed as a counterpoint to the situation in B. subtilis.

Since the Min system of E. coli is by far the best understood Min system, we feel that it is important to provide detailed information on this system. However, we have added an introductory sentence to explain the key function of the Min system (line 46-48).

Line 248: Increasing MinD membrane affinity increases the frequency of minicells - however it is unclear if cells are dividing too much or if it is just a Min mutant (i.e. occasionally dividing at the cell pole vs the middle)? Cell length measurements should be included to clarify this point (Figures 4 and 5).

This information is presented in Fig. 5B (Cell length distribution), which is now Fig. 6B, indicating that the average cell length increases in the tandem alpha helix mutant, a phenotype that is comparable to a MinD knockout. 

Figure 5: I am a bit confused as to whether increasing MinD affinity doesn't lead to a general block in division by MinCD rather than phenocopying a minD null mutant.

Although the tandem alpha helix mutant has a cell length distribution comparable to a minD knockout, the tandem mutant produces much less minicells then the minD knockout, indicating that there is still some cell division regulation.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This is an excellent study by a superb investigator who discovered and is championing the field of migrasomes. This study contains a hidden "gem" - the induction of migrasomes by hypotonicity and how that happens. In summary, an outstanding fundamental phenomenon (migrasomes) en route to becoming transitionally highly significant.

Strengths:

Innovative approach at several levels. Migrasomes - discovered by Dr Yu's group - are an outstanding biological phenomenon of fundamental interest and now of potentially practical value.

Weaknesses:

I feel that the overemphasis on practical aspects (vaccine), however important, eclipses some of the fundamental aspects that may be just as important and actually more interesting. If this can be expanded, the study would be outstanding.

We sincerely thank the reviewer for the encouraging and insightful comments. We fully agree that the fundamental aspects of migrasome biology are of great importance and deserve deeper exploration.

In line with the reviewer’s suggestion, we have expanded our discussion on the basic biology of engineered migrasomes (eMigs). A recent study by the Okochi group at the Tokyo Institute of Technology demonstrated that hypoosmotic stress induces the formation of migrasome-like vesicles, involving cytoplasmic influx and requiring cholesterol for their formation (DOI: 10.1002/1873-3468.14816, February 2024). Building on this, our study provides a detailed characterization of hypoosmotic stressinduced eMig formation, and further compares the biophysical properties of natural migrasomes and eMigs. Notably, the inherent stability of eMigs makes them particularly promising as a vaccine platform.

Finally, we would like to note that our laboratory continues to investigate multiple aspects of migrasome biology. In collaboration with our colleagues, we recently completed a study elucidating the mechanical forces involved in migrasome formation (DOI: 10.1016/j.bpj.2024.12.029), which further complements the findings presented here.

Reviewer #2 (Public review):

Summary:

The authors' report describes a novel vaccine platform derived from a newly discovered organelle called a migrasome. First, the authors address a technical hurdle in using migrasomes as a vaccine platform. Natural migrasome formation occurs at low levels and is labor intensive, however, by understanding the molecular underpinning of migrasome formation, the authors have designed a method to make engineered migrasomes from cultured, cells at higher yields utilizing a robust process. These engineered migrasomes behave like natural migrasomes. Next, the authors immunized mice with migrasomes that either expressed a model peptide or the SARSCoV-2 spike protein. Antibodies against the spike protein were raised that could be boosted by a 2nd vaccination and these antibodies were functional as assessed by an in vitro pseudoviral assay. This new vaccine platform has the potential to overcome obstacles such as cold chain issues for vaccines like messenger RNA that require very stringent storage conditions.

Strengths:

The authors present very robust studies detailing the biology behind migrasome formation and this fundamental understanding was used to form engineered migrasomes, which makes it possible to utilize migrasomes as a vaccine platform. The characterization of engineered migrasomes is thorough and establishes comparability with naturally occurring migrasomes. The biophysical characterization of the migrasomes is well done including thermal stability and characterization of the particle size (important characterizations for a good vaccine).

Weaknesses:

With a new vaccine platform technology, it would be nice to compare them head-tohead against a proven technology. The authors would improve the manuscript if they made some comparisons to other vaccine platforms such as a SARS-CoV-2 mRNA vaccine or even an adjuvanted recombinant spike protein. This would demonstrate a migrasome-based vaccine could elicit responses comparable to a proven vaccine technology. 

We thank the reviewer for the thoughtful evaluation and constructive suggestions, which have helped us strengthen the manuscript. 

Comparison with proven vaccine technologies:

In response to the reviewer’s comment, we now include a direct comparison of the antibody responses elicited by eMig-Spike and a conventional recombinant S1 protein vaccine formulated with Alum. As shown in the revised manuscript (Author response image 1), the levels of S1-specific IgG induced by the eMig-based platform were comparable to those induced by the S1+Alum formulation. This comparison supports the potential of eMigs as a competitive alternative to established vaccine platforms. 

Author response image 1.

eMigrasome-based vaccination showed similar efficacy compared with adjuvanted recombinant spike protein The amount of S1-specific IgG in mouse serum was quantified by ELISA on day 14 after immunization. Mice were either intraperitoneally (i.p.) immunized with recombinant Alum/S1 or intravenously (i.v.) immunized with eM-NC, eM-S or recombinant S1. The administered doses were 20 µg/mouse for eMigrasomes, 10 µg/mouse (i.v.) or 50 µg/mouse (i.p.) for recombinant S1 and 50 µl/mouse for Aluminium adjuvant.

Assessment of antigen integrity on migrasomes:

To address the reviewer’s suggestion regarding antigen integrity, we performed immunoblotting using antibodies against both S1 and mCherry. Two distinct bands were observed: one at the expected molecular weight of the S-mCherry fusion protein, and a higher molecular weight band that may represent oligomerized or higher-order forms of the Spike protein (Figure 5b in the revised manuscript).

Furthermore, we performed confocal microscopy using a monoclonal antibody against Spike (anti-S). Co-localization analysis revealed strong overlap between the mCherry fluorescence and anti-Spike staining, confirming the proper presentation and surface localization of intact S-mCherry fusion protein on eMigs (Figure 5c in the revised manuscript). These results confirm the structural integrity and antigenic fidelity of the Spike protein expressed on eMigs.

Recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

I feel that the overemphasis on practical aspects (vaccine), however important, eclipses some of the fundamental aspects that may be just as important and actually more interesting. If this can be expanded, the study would be outstanding.

I know that the reviewers always ask for more, and this is not the case here. Can the abstract and title be changed to emphasize the science behind migrasome formation, and possibly add a few more fundamental aspects on how hypotonic shock induces migrasomes?

Alternatively, if the authors desire to maintain the emphasis on vaccines, can immunological mechanisms be somewhat expanded in order to - at least to some extent - explain why migrasomes are a better vaccine vehicle?

One way or another, this reviewer is highly supportive of this study and it is really up to the authors and the editor to decide whether my comments are of use or not.

My recommendation is to go ahead with publishing after some adjustments as per above.

We’d like to thank the reviewer for the suggestion. We have changed the title of the manuscript and modified the abstract, emphasizing the fundamental science behind the development of eMigrasome. To gain some immunological information on eMig illucidated antibody responses, we characterized the type of IgG induced by eM-OVA in mice, and compared it to that induced by Alum/OVA. The IgG response to Alum/OVA was dominated by IgG1. Quite differently, eM-OVA induced an even distribution of IgG subtypes, including IgG1, IgG2b, IgG2c, and IgG3 (Figure 4i in the revised manuscript). The ratio between IgG1 and IgG2a/c indicates a Th1 or Th2 type humoral immune response. Thus, eM-OVA immunization induces a balance of Th1/Th2 immune responses.

Reviewer #2 (Recommendations For The Authors):

The study is a very nice exploration of a new vaccine platform. This reviewer believes that a more head-to-head comparison to the current vaccine SARS-CoV-2 vaccine platform would improve the manuscript. This comparison is done with OVA antigen, but this model antigen is not as exciting as a functional head-to-head with a SARS-CoV-2 vaccine.

I think that two other discussion points should be included in the manuscript. First, was the host-cell protein evaluated? If not, I would include that point on how issues of host cell contamination of the migrasome could play a role in the responses and safety of a vaccine. Second, I would discuss antigen incorporation and localization into the platform. For example, the full-length spike being expressed has a native signal peptide and transmembrane domain. The authors point out that a transmembrane domain can be added to display an antigen that does not have one natively expressed, however, without a signal peptide this would not be secreted and localized properly. I would suggest adding a discussion of how a non-native signal peptide would be necessary in addition to a transmembrane domain.

We thank the reviewer for these thoughtful suggestions and fully agree that the points raised are important for the translational development of eMig-based vaccines.

(1) Host cell proteins and potential immunogenicity:

We appreciate the reviewer’s suggestion to consider host cell protein contamination. Considering potential clinical application of eMigrasomes in the future, we will use human cells with low immunogenicity such as HEK-293 or embryonic stem cells (ESCs) to generate eMigrasomes. Also, we will follow a QC that meets the standard of validated EV-based vaccination techniques. 

(2) Antigen incorporation and localization—signal peptide and transmembrane domain:

We also agree with the reviewer’s point that proper surface display of antigens on eMigs requires both a transmembrane domain and a signal peptide for correct trafficking and membrane anchoring. For instance, in the case of full-length Spike protein, the native signal peptide and transmembrane domain ensure proper localization to the plasma membrane and subsequent incorporation into eMigs. In case of OVA, a secretary protein that contains a native signal peptide yet lacks a transmembrane domain, an engineered transmembrane domain is required. For antigens that do not naturally contain these features, both a non-native signal peptide and an artificial transmembrane domain are necessary. We have clarified this point in the revised discussion and explicitly noted the requirement for a signal peptide when engineering antigens for surface display on migrasomes.

Author response:

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

Reviewer #1 (Public review):

Summary

This work performed Raman spectral microscopy at the single-cell level for 15 different culture conditions in E. coli. The Raman signature is systematically analyzed and compared with the proteome dataset of the same culture conditions. With a linear model, the authors revealed correspondence between Raman pattern and proteome expression stoichiometry indicating that spectrometry could be used for inferring proteome composition in the future. With both Raman spectra and proteome datasets, the authors categorized co-expressed genes and illustrated how proteome stoichiometry is regulated among different culture conditions. Co-expressed gene clusters were investigated and identified as homeostasis core, carbon-source dependent, and stationary phase-dependent genes. Overall, the authors demonstrate a strong and solid data analysis scheme for the joint analysis of Raman and proteome datasets.

Strengths and major contributions

(1) Experimentally, the authors contributed Raman datasets of E. coli with various growth conditions.

(2) In data analysis, the authors developed a scheme to compare proteome and Raman datasets. Protein co-expression clusters were identified, and their biological meaning was investigated.

Weaknesses

The experimental measurements of Raman microscopy were conducted at the single-cell level; however, the analysis was performed by averaging across the cells. The author did not discuss if Raman microscopy can used to detect cell-to-cell variability under the same condition.

We thank the reviewer for raising this important point. Though this topic is beyond the scope of our study, some of our authors have addressed the application of single-cell Raman spectroscopy to characterizing phenotypic heterogeneity in individual Staphylococcus aureus cells in another paper (Kamei et al., bioRxiv, doi: 10.1101/2024.05.12.593718). Additionally, one of our authors demonstrated that single-cell RNA sequencing profiles can be inferred from Raman images of mouse cells (Kobayashi-Kirschvink et al., Nat. Biotechnol. 42, 1726–1734, 2024). Therefore, detecting cell-to-cell variability under the same conditions has been shown to be feasible. Whether averaging single-cell Raman spectra is necessary depends on the type of analysis and the available dataset. We will discuss this in more detail in our response to Comment (1) by Reviewer #1 (Recommendation for the authors).

Discussion and impact on the field

Raman signature contains both proteomic and metabolomic information and is an orthogonal method to infer the composition of biomolecules. It has the advantage that single-cell level data could be acquired and both in vivo and in vitro data can be compared. This work is a strong initiative for introducing the powerful technique to systems biology and providing a rigorous pipeline for future data analysis.

Reviewer #2 (Public review):

Summary and strengths:

Kamei et al. observe the Raman spectra of a population of single E. coli cells in diverse growth conditions. Using LDA, Raman spectra for the different growth conditions are separated. Using previously available protein abundance data for these conditions, a linear mapping from Raman spectra in LDA space to protein abundance is derived. Notably, this linear map is condition-independent and is consequently shown to be predictive for held-out growth conditions. This is a significant result and in my understanding extends the earlier Raman to RNA connection that has been reported earlier.

They further show that this linear map reveals something akin to bacterial growth laws (ala Scott/Hwa) that the certain collection of proteins shows stoichiometric conservation, i.e. the group (called SCG - stoichiometrically conserved group) maintains their stoichiometry across conditions while the overall scale depends on the conditions. Analyzing the changes in protein mass and Raman spectra under these conditions, the abundance ratios of information processing proteins (one of the large groups where many proteins belong to "information and storage" - ISP that is also identified as a cluster of orthologous proteins) remain constant. The mass of these proteins deemed, the homeostatic core, increases linearly with growth rate. Other SCGs and other proteins are condition-specific.

Notably, beyond the ISP COG the other SCGs were identified directly using the proteome data. Taking the analysis beyond they then how the centrality of a protein - roughly measured as how many proteins it is stoichiometric with - relates to function and evolutionary conservation. Again significant results, but I am not sure if these ideas have been reported earlier, for example from the community that built protein-protein interaction maps.

As pointed out, past studies have revealed that the function, essentiality, and evolutionary conservation of genes are linked to the topology of gene networks, including protein-protein interaction networks. However, to the best of our knowledge, their linkage to stoichiometry conservation centrality of each gene has not yet been established.

Previously analyzed networks, such as protein-protein interaction networks, depend on known interactions. Therefore, as our understanding of the molecular interactions evolves with new findings, the conclusions may change. Furthermore, analysis of a particular interaction network cannot account for effects from different types of interactions or multilayered regulations affecting each protein species.

In contrast, the stoichiometry conservation network in this study focuses solely on expression patterns as the net result of interactions and regulations among all types of molecules in cells. Consequently, the stoichiometry conservation networks are not affected by the detailed knowledge of molecular interactions and naturally reflect the global effects of multilayered interactions. Additionally, stoichiometry conservation networks can easily be obtained for non-model organisms, for which detailed molecular interaction information is usually unavailable. Therefore, analysis with the stoichiometry conservation network has several advantages over existing methods from both biological and technical perspectives.

We added a paragraph explaining this important point to the Discussion section, along with additional literature.

Finally, the paper built a lot of "machinery" to connect ¥Omega_LE, built directly from proteome, and ¥Omega_B, built from Raman, spaces. I am unsure how that helps and have not been able to digest the 50 or so pages devoted to this.

The mathematical analyses in the supplementary materials form the basis of the argument in the main text. Without the rigorous mathematical discussions, Fig. 6E — one of the main conclusions of this study — and Fig. 7 could never be obtained. Therefore, we believe the analyses are essential to this study. However, we clarified why each analysis is necessary and significant in the corresponding sections of the Results to improve the manuscript's readability.

Please see our responses to comments (2) and (7) by Reviewer #1 (Recommendations for the authors) and comments (5) and (6) by Reviewer #2 (Recommendations for the authors).

Strengths:

The rigorous analysis of the data is the real strength of the paper. Alongside this, the discovery of SCGs that are condition-independent and that are condition-dependent provides a great framework.

Weaknesses:

Overall, I think it is an exciting advance but some work is needed to present the work in a more accessible way.

We edited the main text to make it more accessible to a broader audience. Please see our responses to comments (2) and (7) by Reviewer #1 (Recommendations for the authors) and comments (5) and (6) by Reviewer #2 (Recommendations for the authors).

Reviewer #1 (Recommendations for the authors):

(1) The Raman spectral data is measured from single-cell imaging. In the current work, most of the conclusions are from averaged data. From my understanding, once the correspondence between LDA and proteome data is established (i.e. the matrix B) one could infer the single-cell proteome composition from B. This would provide valuable information on how proteome composition fluctuates at the single-cell level.

We can calculate single-cell proteomes from single-cell Raman spectra in the manner suggested by the reviewer. However, we cannot evaluate the accuracy of their estimation without single-cell proteome data under the same environmental conditions. Likewise, we cannot verify variations of estimated proteomes of single cells. Since quantitatively accurate single-cell proteome data is unavailable, we concluded that addressing this issue was beyond the scope of this study.

Nevertheless, we agree with the reviewer that investigating how proteome composition fluctuates at the single-cell level based on single-cell Raman spectra is an intriguing direction for future research. In this regard, some of our authors have studied the phenotypic heterogeneity of Staphylococcus aureus cells using single-cell Raman spectra in another paper (Kamei et al., bioRxiv, doi: 10.1101/2024.05.12.593718), and one of our authors has demonstrated that single-cell RNA sequencing profiles can be inferred from Raman images of mouse cells (Kobayashi-Kirschvink et al., Nat. Biotechnol. 42, 1726–1734, 2024). Therefore, it is highly plausible that single-cell Raman spectroscopy can also characterize proteomic fluctuations in single cells. We have added a paragraph to the Discussion section to highlight this important point.

(2) The establishment of matrix B is quite confusing for readers who only read the main text. I suggest adding a flow chart in Figure 1 to explain the data analysis pipeline, as well as state explicitly what is the dimension of B, LDA matrix, and proteome matrix.

We thank the reviewer for the suggestion. Following the reviewer's advice, we have explicitly stated the dimensions of the vectors and matrices in the main text. We have also added descriptions of the dimensions of the constructed spaces. Rather than adding another flow chart to Figure 1, we added a new table (Table 1) to explain the various symbols representing vectors and matrices, thereby improving the accessibility of the explanation.

(3) One of the main contributions for this work is to demonstrate how proteome stoichiometry is regulated across different conditions. A total of m=15 conditions were tested in this study, and this limits the rank of LDA matrix as 14. Therefore, maximally 14 "modes" of differential composition in a proteome can be detected.

As a general reader, I am wondering in the future if one increases or decreases the number of conditions (say m=5 or m=50) what information can be extracted? It is conceivable that increasing different conditions with distinct cellular physiology would be beneficial to "explore" different modes of regulation for cells. As proof of principle, I am wondering if the authors could test a lower number (by sub-sampling from m=15 conditions, e.g. picking five of the most distinct conditions) and see how this would affect the prediction of proteome stoichiometry inference.

We thank the reviewer for bringing an important point to our attention. To address the issue raised, we conducted a new subsampling analysis (Fig. S14).

As we described in the main text (Fig. 6E) and the supplementary materials, the m x m orthogonal matrix, Θ, represents to what extent the two spaces Ω_LE and Ω_B are similar (m is the number of conditions; in our main analysis, m = 15). Thus, the low-dimensional correspondence between the two spaces connected by an orthogonal transformation, such as an m-dimensional rotation, can be evaluated by examining the elements of the matrix Θ. Specifically, large off-diagonal elements of the matrix  mix higher dimensions and lower dimensions, making the two spaces spanned by the first few major axes appear dissimilar. Based on this property, we evaluated the vulnerability of the low-dimensional correspondence between Ω_LE and Ω_B to the reduced number of conditions by measuring how close Θ was to the identity matrix when the analysis was performed on the subsampled datasets.

In the new figure (Fig. S14), we first created all possible smaller condition sets by subsampling the conditions. Next, to evaluate the closeness between the matrix Θ and the identity matrix for each smaller condition set, we generated 10,000 random orthogonal matrices of the same size as . We then evaluated the probability of obtaining a higher level of low-dimensional correspondence than that of the experimental data by chance (see section 1.8 of the Supplementary Materials). This analysis was already performed in the original manuscript for the non-subsampled case (m = 15) in Fig. S9C; the new analysis systematically evaluates the correspondence for the subsampled datasets.

The results clearly show that low-dimensional correspondence is more likely to be obtained with more conditions (Fig. S14). In particular, when the number of conditions used in the analysis exceeds five, the median of the probability that random orthogonal matrices were closer to the identity matrix than the matrix Θ calculated from subsampled experimental data became lower than 10^-4. This analysis provides insight into the number of conditions required to find low-dimensional correspondence between Ω_LE and Ω_B.

What conditions are used in the analysis can change the low-dimensional structures of Ω_LE and Ω_B . Therefore, it is important to clarify whether including more conditions in the analysis reduces the dependence of the low-dimensional structures on conditions. We leave this issue as a subject for future study. This issue relates to the effective dimensionality of omics profiles needed to establish the diverse physiological states of cells across conditions. Determining the minimum number of conditions to attain the condition-independent low-dimensional structures of Ω_LE and Ω_B would provide insight into this fundamental problem. Furthermore, such an analysis would identify the range of applications of Raman spectra as a tool for capturing macroscopic properties of cells at the system level.

We now discuss this point in the Discussion section, referring to this analysis result (Fig. S14). Please also see our reply to the comment (1) by Reviewer #2 (Recommendations for the authors).

(4) In E. coli cells, total proteome is in mM concentration while the total metabolites are between 10 to 100 mM concentration. Since proteins are large molecules with more functional groups, they may contribute to more Raman signal (per molecules) than metabolites. Still, the meaningful quantity here is the "differential Raman signal" with different conditions, not the absolute signal. I am wondering how much percent of differential Raman signature are from proteome and how much are from metabolome.

It is an important and interesting question to what extent changes in the proteome and metabolome contribute to changes in Raman spectra. Though we concluded that answering this question is beyond the scope of this study, we believe it is an important topic for future research.

Raman spectral patterns convey the comprehensive molecular composition spanning the various omics layers of target cells. Changes in the composition of these layers can be highly correlated, and identifying their contributions to changes in Raman spectra would provide insight into the mutual correlation of different omics layers. Addressing the issue raised by the reviewer would expand the applications of Raman spectroscopy and highlight the advantage of cellular Raman spectra as a means of capturing comprehensive multi-omics information.

We note that some studies have evaluated the contributions of proteins, lipids, nucleic acids, and glycogen to the Raman spectra of mammalian cells and how these contributions change in different states (e.g., Mourant et al., J Biomed Opt, 10(3), 031106, 2005). Additionally, numerous studies have imaged or quantified metabolites in various cell types (see, for example, Cutshaw et al., Chemical Reviews, 123(13), 8297–8346, 2023, for a comprehensive review). Extending these approaches to multiple omics layers in future studies would help resolve the issue raised by the reviewer.

(5) It is known that E. coli cells in different conditions have different cell sizes, where cell width increases with carbon source quality and growth rate. Does this effect be normalized when processing the Raman signal?

Each spectrum was normalized by subtracting the average and dividing it by the standard deviation. This normalization minimizes the differences in signal intensities due to different cell sizes and densities. This information is shown in the Materials and Methods section of the Supplementary Materials.

(6) I have a question about interpretation of the centrality index. A higher centrality indicates the protein expression pattern is more aligned with the "mainstream" of the other proteins in the proteome. However, it is possible that the proteome has multiple" mainstream modes" (with possibly different contributions in magnitudes), and the centrality seems to only capture the "primary mode". A small group of proteins could all have low centrality but have very consistent patterns with high conservation of stoichiometry. I wondering if the author could discuss and clarify with this.

We thank the reviewer for drawing our attention to the insufficient explanation in the original manuscript. First, we note that stoichiometry conserving protein groups are not limited to those composed of proteins with high stoichiometry conservation centrality. The SCGs 2–5 are composed of proteins that strongly conserve stoichiometry within each group but have low stoichiometry conservation centrality (Fig. 5A, 5K, 5L, and 7A). In other words, our results demonstrate the existence of the "primary mainstream mode" (SCG 1, i.e., the homeostatic core) and condition-specific "non-primary mainstream modes" (SCGs 2–5). These primary and non-primary modes are distinguishable by their position along the axis of stoichiometry conservation centrality (Fig. 5A, 5K, and 5L).

However, a single one-dimensional axis (centrality) cannot capture all characteristics of stoichiometry-conserving architecture. In our case, the "non-primary mainstream modes" (SCGs 2–5) were distinguished from each other by multiple csLE axes.

To clarify this point, we modified the first paragraph of the section where we first introduce csLE (Revealing global stoichiometry conservation architecture of the proteomes with csLE). We also added a paragraph to the Discussion section regarding the condition-specific SCGs 2–5.

(7) Figures 3, 4, and 5A-I are analyses on proteome data and are not related to Raman spectral data. I am wondering if this part of the analysis can be re-organized and not disrupt the mainline of the manuscript.

We agree that the structure of this manuscript is complicated. Before submitting this manuscript to eLife, we seriously considered reorganizing it. However, we concluded that this structure was most appropriate because our focus on stoichiometry conservation cannot be explained without analyzing the coefficients of the Raman-proteome correspondence using COG classification (see Fig. 3; note that Fig. 3A relates to Raman data). This analysis led us to examine the global stoichiometry conservation architecture of proteomes (Figs. 4 and 5) and discover the unexpected similarity between the low-dimensional structures of Ω_LE and Ω_B

Therefore, we decided to keep the structure of the manuscript as it is. To partially resolve this issue, however, we added references to Fig. S1, the diagram of this paper’s mainline, to several places in the main text so that readers can more easily grasp the flow of the manuscript.

(8) Supplementary Equation (2.6) could be wrong. From my understanding of the coordinate transformation definition here, it should be [w1 ... ws] X := RHS terms in big parenthesis.

We checked the equation and confirmed that it is correct.

Reviewer #2 (Recommendations for the authors):

(1) The first main result or linear map between raman and proteome linked via B is intriguing in the sense that the map is condition-independent. A speculative question I have is if this relationship may become more complex or have more condition-dependent corrections as the number of conditions goes up. The 15 or so conditions are great but it is not clear if they are often quite restrictive. For example, they assume an abundance of most other nutrients. Now if you include a growth rate decrease due to nitrogen or other limitations, do you expect this to work?

In our previous paper (Kobayashi-Kirschvink et al., Cell Systems 7(1): 104–117.e4, 2018), we statistically demonstrated a linear correspondence between cellular Raman spectra and transcriptomes for fission yeast under 10 environmental conditions. These conditions included nutrient-rich and nutrient-limited conditions, such as nitrogen limitation. Since the Raman-transcriptome correspondence was only statistically verified in that study, we analyzed the data from the standpoint of stoichiometry conservation in this study. The results (Fig. S11 and S12) revealed a correspondence in lower dimensions similar to that observed in our main results. In addition, similar correspondences were obtained even for different E. coli strains under common culture conditions (Fig. S11 and S12). Therefore, it is plausible that the stoichiometry-conservation low-dimensional correspondence between Raman and gene expression profiles holds for a wide range of external and internal perturbations.

We agree with the reviewer that it is important to understand how Raman-omics correspondences change with the number of conditions. To address this issue, we examined how the correspondence between Ω_LE and Ω_B changes by subsampling the conditions used in the analysis. We focused on , which was introduced in Fig. 5E, because the closeness of Θ to the identity matrix represents correspondence precision. We found a general trend that the low-dimensional correspondence becomes more precise as the number of conditions increases (Fig. S14). This suggests that increasing the number of conditions generally improves the correspondence rather than disrupting it.

We added a paragraph to the Discussion section addressing this important point. Please also refer to our response to Comment (3) of Reviewer #1 (Recommendations for the authors).

(2) A little more explanation in the text for 3C/D would help. I am imagining 3D is the control for 3C. Minor comment - 3B looks identical to S4F but the y-axis label is different.

We thank the reviewer for pointing out the insufficient explanation of Fig. 3C and 3D in the main text. Following this advice, we added explanations of these plots to the main text. We also added labels ("ISP COG class" and "non-ISP COG class") to the top of these two figures.

Fig. 3B and S4F are different. For simplicity, we used the Pearson correlation coefficient in Fig. 3B. However, cosine similarity is a more appropriate measure for evaluating the degree of conservation of abundance ratios. Thus, we presented the result using cosine similarity in a supplementary figure (Fig. S4F). Please note that each point in Fig. S4F is calculated between proteome vectors of two conditions. The dimension of each proteome vector is the number of genes in each COG class.

(3) Can we see a log-log version of 4C to see how the low-abundant proteins are behaving? In fact, the same is in part true for Figure 3A.

We added the semi-log version of the graph for SCG1 (the homeostatic core) in Fig. 4C to make low-abundant proteins more visible. Please note that the growth rates under the two stationary-phase conditions were zero; therefore, plotting this graph in log-log format is not possible.

Fig. 3A cannot be shown as a log-log plot because many of the coefficients are negative. The insets in the graphs clarify the points near the origin.

(4) In 5L, how should one interpret the other dots that are close to the center but not part of the SCG1? And this theme continues in 6ACD and 7A.

The SCGs were obtained by setting a cosine similarity threshold. Therefore, proteins that are close to SCG 1 (the homeostatic core) but do not belong to it have a cosine similarity below the threshold with any protein in SCG 1. Fig. 7 illustrates the expression patterns of the proteins in question.

(5) Finally, I do not fully appreciate the whole analysis of connecting ¥Omega_csLE and ¥Omega_B and plots in 6 and 7. This corresponds to a lot of linear algebra in the 50 or so pages in section 1.8 in the supplementary. If the authors feel this is crucial in some way it needs to be better motivated and explained. I philosophically appreciate developing more formalism to establish these connections but I did not understand how this (maybe even if in the future) could lead to a new interpretation or analysis or theory.

The mathematical analyses included in the supplementary materials are important for readers who are interested in understanding the mathematics behind our conclusions. However, we also thought these arguments were too detailed for many readers when preparing the original submission and decided to show them in the supplemental materials.

To better explain the motivation behind the mathematical analyses, we revised the section “Representing the proteomes using the Raman LDA axes”.

Please also see our reply to the comment (6) by Reviewer #2 (Recommendations for the authors) below.

(6) Along the lines of the previous point, there seems to be two separate points being made: a) there is a correspondence between Raman and proteins, and b) we can use the protein data to look at centrality, generality, SCGs, etc. And the two don't seem to be linked until the formalism of ¥Omegas?

The reviewer is correct that we can calculate and analyze some of the quantities introduced in this study, such as stoichiometry conservation centrality and expression generality, without Raman data. However, it is difficult to justify introducing these quantities without analyzing the correspondence between the Raman and proteome profiles. Moreover, the definition of expression generality was derived from the analysis of Raman-proteome correspondence (see section 2.2 of the Supplementary Materials). Therefore, point b) cannot stand alone without point a) from its initial introduction.

To partially improve the readability and resolve the issue of complicated structure of this manuscript, we added references to Fig. S1, which is a diagram of the paper’s mainline, to several places in the main text. Please also see our reply to the comment (7) by Reviewer #1 (Recommendations for the authors).

Author response:

We would like to thank the three Reviewers for their thoughtful comments and detailed feedback. We are pleased to hear that the Reviewers found our paper to be “providing more direct evidence for the role of signals in different frequency bands related to predictability and surprise” (R1), “well-suited to test evidence for predictive coding versus alternative hypotheses” (R2), and “timely and interesting” (R3).

We perceive that the reviewers have an overall positive impression of the experiments and analyses, but find the text somewhat dense and would like to see additional statistical rigor, as well as in some cases additional analyses to be included in supplementary material. We therefore here provide a provisional letter addressing revisions we have already performed and outlining the revision we are planning point-by-point. We begin each enumerated point with the Reviewer’s quoted text and our responses to each point are made below.

Reviewer 1:

(1) Introduction:

The authors write in their introduction: "H1 further suggests a role for θ oscillations in prediction error processing as well." Without being fleshed out further, it is unclear what role this would be, or why. Could the authors expand this statement?”

We have edited the text to indicate that theta-band activity has been related to prediction error processing as an empirical observation, and must regrettably leave drawing inferences about its functional role to future work, with experiments designed specifically to draw out theta-band activity.

(2) Limited propagation of gamma band signals:

Some recent work (e.g. https://www.cell.com/cell-reports/fulltext/S2211-1247(23)00503-X) suggests that gamma-band signals reflect mainly entrainment of the fast-spiking interneurons, and don't propagate from V1 to downstream areas. Could the authors connect their findings to these emerging findings, suggesting no role in gamma-band activity in communication outside of the cortical column?”

We have not specifically claimed that gamma propagates between columns/areas in our recordings, only that it synchronizes synaptic current flows between laminar layers within a column/area. We nonetheless suggest that gamma can locally synchronize a column, and potentially local columns within an area via entrainment of local recurrent spiking, to update an internal prediction/representation upon onset of a prediction error. We also point the Reviewer to our Discussion section, where we state that our results fit with a model “whereby θ oscillations synchronize distant areas, enabling them to exchange relevant signals during cognitive processing.” In our present work, we therefore remain agnostic about whether theta or gamma or both (or alternative mechanisms) are at play in terms of how prediction error signals are transmitted between areas.

(3) Paradigm:

While I agree that the paradigm tests whether a specific type of temporal prediction can be formed, it is not a type of prediction that one would easily observe in mice, or even humans. The regularity that must be learned, in order to be able to see a reflection of predictability, integrates over 4 stimuli, each shown for 500 ms with a 500 ms blank in between (and a 1000 ms interval separating the 4th stimulus from the 1st stimulus of the next sequence). In other words, the mouse must keep in working memory three stimuli, which partly occurred more than a second ago, in order to correctly predict the fourth stimulus (and signal a 1000 ms interval as evidence for starting a new sequence).

A problem with this paradigm is that positive findings are easier to interpret than negative findings. If mice do not show a modulation to the global oddball, is it because "predictive coding" is the wrong hypothesis, or simply because the authors generated a design that operates outside of the boundary conditions of the theory? I think the latter is more plausible. Even in more complex animals, (eg monkeys or humans), I suspect that participants would have trouble picking up this regularity and sequence, unless it is directly task-relevant (which it is not, in the current setting). Previous experiments often used simple pairs (where transitional probability was varied, eg, Meyer and Olson, PNAS 2012) of stimuli that were presented within an intervening blank period. Clearly, these regularities would be a lot simpler to learn than the highly complex and temporally spread-out regularity used here, facilitating the interpretation of negative findings (especially in early cortical areas, which are known to have relatively small temporal receptive fields).

I am, of course, not asking the authors to redesign their study. I would like to ask them to discuss this caveat more clearly, in the Introduction and Discussion, and situate their design in the broader literature. For example, Jeff Gavornik has used much more rapid stimulus designs and observed clear modulations of spiking activity in early visual regions. I realize that this caveat may be more relevant for the spiking paper (which does not show any spiking activity modulation in V1 by global predictability) than for the current paper, but I still think it is an important general caveat to point out.”

We appreciate the Reviewer’s concern about working memory limitations in mice. Our paradigm and training followed on from previous paradigms such as Gavornik and Bear (2014), in which predictive effects were observed in mouse V1 with presentation times of 150ms and interstimulus intervals of 1500ms. In addition, we note that Jamali et al. (2024) recently utilized a similar global/local paradigm in the auditory domain with inter-sequence intervals as long as 28-30 seconds, and still observed effects of a predicted sequence (https://elifesciences.org/articles/102702). For the revised manuscript, we plan to expand on this in the Discussion section.

That being said, as the Reviewer also pointed out, this would be a greater concern had we not found any positive findings in our study. However, even with the rather long sequence periods we used, we did find positive evidence for predictive effects, supporting the use of our current paradigm. We agree with the reviewer that these positive effects are easier to interpret than negative effects, and plan to expand upon this in the Discussion when we resubmit.

(4) Reporting of results:

I did not see any quantification of the strength of evidence of any of the results, beyond a general statement that all reported results pass significance at an alpha=0.01 threshold. It would be informative to know, for all reported results, what exactly the p-value of the significant cluster is; as well as for which performed tests there was no significant difference.”

For the revised manuscript, we can include the p-values after cluster-based testing for each significant cluster, as well as show data that passes a more stringent threshold of p<0.001 (1/1000) or p<0.005 (1/200) rather than our present p<0.01 (1/100).

(5) Cluster test:

The authors use a three-dimensional cluster test, clustering across time, frequency, and location/channel. I am wondering how meaningful this analytical approach is. For example, there could be clusters that show an early difference at some location in low frequencies, and then a later difference in a different frequency band at another (adjacent) location. It seems a priori illogical to me to want to cluster across all these dimensions together, given that this kind of clustering does not appear neurophysiologically implausible/not meaningful. Can the authors motivate their choice of three-dimensional clustering, or better, facilitating interpretability, cluster eg at space and time within specific frequency bands (2d clustering)?”

We are happy to include a 3D plot of a time-channel-frequency cluster in the revised manuscript to clarify our statistical approach for the reviewer. We consider our current three-dimensional cluster-testing an “unsupervised” way of uncovering significant contrasts with no theory-driven assumptions about which bounded frequency bands or layers do what.

Reviewer 2:

Sennesh and colleagues analyzed LFP data from 6 regions of rodents while they were habituated to a stimulus sequence containing a local oddball (xxxy) and later exposed to either the same (xxxY) or a deviant global oddball (xxxX). Subsequently, they were exposed to a controlled random sequence (XXXY) or a controlled deterministic sequence (xxxx or yyyy). From these, the authors looked for differences in spectral properties (both oscillatory and aperiodic) between three contrasts (only for the last stimulus of the sequence).

(1) Deviance detection: unpredictable random (XXXY) versus predictable habituation (xxxy)

(2) Global oddball: unpredictable global oddball (xxxX) versus predictable deterministic (xxxx), and

(3) "Stimulus-specific adaptation:" locally unpredictable oddball (xxxY) versus predictable deterministic (yyyy).

They found evidence for an increase in gamma (and theta in some cases) for unpredictable versus predictable stimuli, and a reduction in alpha/beta, which they consider evidence towards the "predictive routing" scheme.

While the dataset and analyses are well-suited to test evidence for predictive coding versus alternative hypotheses, I felt that the formulation was ambiguous, and the results were not very clear. My major concerns are as follows:”

We appreciate the reviewer’s concerns and outline how we will address them below:

(1) The authors set up three competing hypotheses, in which H1 and H2 make directly opposite predictions. However, it must be noted that H2 is proposed for spatial prediction, where the predictability is computed from the part of the image outside the RF. This is different from the temporal prediction that is tested here. Evidence in favor of H2 is readily observed when large gratings are presented, for which there is substantially more gamma than in small images. Actually, there are multiple features in the spectral domain that should not be conflated, namely (i) the transient broadband response, which includes all frequencies, (ii) contribution from the evoked response (ERP), which is often in frequencies below 30 Hz, (iii) narrow-band gamma oscillations which are produced by large and continuous stimuli (which happen to be highly predictive), and (iv) sustained low-frequency rhythms in theta and alpha/beta bands which are prominent before stimulus onset and reduce after ~200 ms of stimulus onset. The authors should be careful to incorporate these in their formulation of PC, and in particular should not conflate narrow-band and broadband gamma.”

We have clarified in the manuscript that while the gamma-as-prediction hypothesis (our H2) was originally proposed in a spatial prediction domain, further work (specifically Singer (2021)) has extended the hypothesis to cover temporal-domain predictions as well.

To address the reviewer’s point about multiple features in the spectral domain: Our analysis has specifically separated aperiodic components using FOOOF analysis (Supp. Fig. 1) and explicitly fit and tested aperiodic vs. periodic components (Supp. Figs 1&2). We did not find strong effects in the aperiodic components but did in the periodic components (Supp. Fig. 2), allowing us to be more confident in our conclusions in terms of genuine narrow-band oscillations. In the revised manuscript, we will include analysis of the pre-stimulus time window to address the reviewer’s point (iv) on sustained low frequency oscillations.

(2) My understanding is that any aspect of predictive coding must be present before the onset of stimulus (expected or unexpected). So, I was surprised to see that the authors have shown the results only after stimulus onset. For all figures, the authors should show results from -500 ms to 500 ms instead of zero to 500 ms.

In our revised manuscript we will include a pre-stimulus analysis and supplementary figures with time ranges from -500ms to 500ms. We have only refrained from doing so in the initial manuscript because our paradigm’s short interstimulus interval makes it difficult to interpret whether activity in the ISI reflects post-stimulus dynamics or pre-stimulus prediction. Nonetheless, we can easily show that in our paradigm, alpha/beta-band activity is elevated in the interstimulus activity after the offset of the previous stimulus, assuming that we baseline to the pre-trial period.

(3) In many cases, some change is observed in the initial ~100 ms of stimulus onset, especially for the alpha/beta and theta ranges. However, the evoked response contributes substantially in the transient period in these frequencies, and this evoked response could be different for different conditions. The authors should show the evoked responses to confirm the same, and if the claim really is that predictions are carried by genuine "oscillatory" activity, show the results after removing the ERP (as they had done for the CSD analysis).

We have included an extra sentence in our Materials and Methods section clarifying that the evoked potential/ERP was removed in our existing analyses, prior to performing the spectral decomposition of the LFP signal. We also note that the FOOOF analysis we applied separates aperiodic components of the spectral signal from the strictly oscillatory ones.

In our revised manuscript we will include an analysis of the evoked responses as suggested by the reviewer.

(4) I was surprised by the statistics used in the plots. Anything that is even slightly positive or negative is turning out to be significant. Perhaps the authors could use a more stringent criterion for multiple comparisons?

As noted above to Reviewer 1 (point 4), we are happy to include supplemental figures in our resubmission showing the effects on our results of setting the statistical significance threshold with considerably greater stringency.

(5) Since the design is blocked, there might be changes in global arousal levels. This is particularly important because the more predictive stimuli in the controlled deterministic stimuli were presented towards the end of the session, when the animal is likely less motivated. One idea to check for this is to do the analysis on the 3rd stimulus instead of the 4th? Any general effect of arousal/attention will be reflected in this stimulus.

In order to check for the brain-wide effects of arousal, we plan to perform similar analyses to our existing ones on the 3rd stimulus in each block, rather than just the 4th “oddball” stimulus. Clusters that appear significantly contrasting in both the 3rd and 4th stimuli may be attributable to arousal.  We will also analyze pupil size as an index of arousal to check for arousal differences between conditions in our contrasts, possibly stratifying our data before performing comparisons to equalize pupil size within contrasts. We plan to include these analyses in our resubmission.

(6) The authors should also acknowledge/discuss that typical stimulus presentation/attention modulation involves both (i) an increase in broadband power early on and (ii) a reduction in low-frequency alpha/beta power. This could be just a sensory response, without having a role in sending prediction signals per se. So the predictive routing hypothesis should involve testing for signatures of prediction while ruling out other confounds related to stimulus/cognition. It is, of course, very difficult to do so, but at the same time, simply showing a reduction in low-frequency power coupled with an increase in high-frequency power is not sufficient to prove PR.

Since many different predictive coding and predictive processing hypotheses make very different hypotheses about how predictions might encoded in neurophysiological recordings, we have focused on prediction error encoding in this paper.

For the hypothesis space we have considered (H1-H3), each hypothesis makes clearly distinguishable predictions about the spectral response during the time period in the task when prediction errors should be present. As noted by the reviewer, a transient increase in broadband frequencies would be a signature of H3. Changes to oscillatory power in the gamma band in distinct directions (e.g., increasing or decreasing with prediction error) would support either H1 and H2, depending on the direction of change. We believe our data, especially our use of FOOOF analysis and separation of periodic from aperiodic components, coupled to the three experimental contrasts, speaks clearly in favor of the Predictive Routing model, but we do not claim we have “proved” it. This study provides just one datapoint, and we will acknowledge this in our revised Discussion in our resubmission.

(7) The CSD results need to be explained better - you should explain on what basis they are being called feedforward/feedback. Was LFP taken from Layer 4 LFP (as was done by van Kerkoerle et al, 2014)? The nice ">" and "<" CSD patterns (Figure 3B and 3F of their paper) in that paper are barely observed in this case, especially for the alpha/beta range.

We consider a feedforward pattern as flowing from L4 outwards to L2/3 and L5/6, and a feedback pattern as flowing in the opposite direction, from L1 and L6 to the middle layers. We will clarify this in the revised manuscript.

Since gamma-band oscillations are strongest in L2/3, we re-epoched LFPs to the oscillation troughs in L2/3 in the initial manuscript. We can include in the revised manuscript equivalent plots after finding oscillation troughs in L4 instead, as well as calculating the difference in trough times within-band between layers to quantify the transmission delay and add additional rigor to our feedforward vs. feedback interpretation of the CSD data.

(8) Figure 4a-c, I don't see a reduction in the broadband signal in a compared to b in the initial segment. Maybe change the clim to make this clearer?

We are looking into the clim/colorbar and plot-generation code to figure out the visibility issue that the Reviewer has kindly pointed out to us.

(9) Figure 5 - please show the same for all three frequency ranges, show all bars (including the non-significant ones), and indicate the significance (p-values or by *, **, ***, etc) as done usually for bar plots.

We will add the requested bar-plots for all frequency ranges, though we note that the bars given here are the results of adding up the spectral power in the channel-time-frequency clusters that already passed significance tests and that adding secondary significance tests here may not prove informative.

(10) Their claim of alpha/beta oscillations being suppressed for unpredictable conditions is not as evident. A figure akin to Figure 5 would be helpful to see if this assertion holds.

As noted above, we will include the requested bar plot, as well as examining alpha/beta in the pre-stimulus time-series rather than after the onset of the oddball stimulus.

(11) To investigate the prediction and violation or confirmation of expectation, it would help to look at both the baseline and stimulus periods in the analyses.

We will include for the Reviewer’s edification a supplementary figure showing the spectrograms for the baseline and full-trial periods to look at the difference between baseline and prestimulus expectation.

Reviewer 3:

Summary:

In their manuscript entitled "Ubiquitous predictive processing in the spectral domain of sensory cortex", Sennesh and colleagues perform spectral analysis across multiple layers and areas in the visual system of mice. Their results are timely and interesting as they provide a complement to a study from the same lab focussed on firing rates, instead of oscillations. Together, the present study argues for a hypothesis called predictive routing, which argues that non-predictable stimuli are gated by Gamma oscillations, while alpha/beta oscillations are related to predictions.

Strengths:

(1) The study contains a clear introduction, which provides a clear contrast between a number of relevant theories in the field, including their hypotheses in relation to the present data set.

(2) The study provides a systematic analysis across multiple areas and layers of the visual cortex.”

We thank the Reviewer for their kind comments.

Weaknesses:

(1) It is claimed in the abstract that the present study supports predictive routing over predictive coding; however, this claim is nowhere in the manuscript directly substantiated. Not even the differences are clearly laid out, much less tested explicitly. While this might be obvious to the authors, it remains completely opaque to the reader, e.g., as it is also not part of the different hypotheses addressed. I guess this result is meant in contrast to reference 17, by some of the same authors, which argues against predictive coding, while the present work finds differences in the results, which they relate to spectral vs firing rate analysis (although without direct comparison).

We agree that in this manuscript we should restrict ourselves to the hypotheses that were directly tested. We have revised our abstract accordingly,  and softened our claim to note only that our LFP results are compatible with predictive routing.

(2) Most of the claims about a direction of propagation of certain frequency-related activities (made in the context of Figures 2-4) are - to the eyes of the reviewer - not supported by actual analysis but glimpsed from the pictures, sometimes, with very little evidence/very small time differences to go on. To keep these claims, proper statistical testing should be performed.

In our revised manuscript, we will either substantiate (with quantification of CSD delays between layers) or soften the claims about feedforward/feedback direction of flow within the cortical column.

(3) Results from different areas are barely presented. While I can see that presenting them in the same format as Figures 2-4 would be quite lengthy, it might be a good idea to contrast the right columns (difference plots) across areas, rather than just the overall averages.

In our revised manuscript we will gladly include a supplementary figure showing the right-column difference plots across areas, in order to make sure to include aspects of our dataset that span up and down the cortical hierarchy.

(4) Statistical testing is treated very generally, which can help to improve the readability of the text; however, in the present case, this is a bit extreme, with even obvious tests not reported or not even performed (in particular in Figure 5).

We appreciate the Reviewer’s concern for statistical rigor, and as noted to the other reviewers, we can add different levels of statistical description and describe the p-values associated with specific clusters. Regarding Figure 5, we must protest as the bar heights were computed came from clusters already subjected to statistical testing and found significant.  We could add a supplementary figure which considers untested narrowband activity and tests it only in the “bar height” domain, if the Reviewer would like.

(5) The description of the analysis in the methods is rather short and, to my eye, was missing one of the key descriptions, i.e., how the CSD plots were baselined (which was hinted at in the results, but, as far as I know, not clearly described in the analysis methods). Maybe the authors could section the methods more to point out where this is discussed.

We have added some elaboration to our Materials and Methods section, especially to specify that CSD, having physical rather than arbitrary units, does not require baselining.

(6) While I appreciate the efforts of the authors to formulate their hypotheses and test them clearly, the text is quite dense at times. Partly this is due to the compared conditions in this paradigm; however, it would help a lot to show a visualization of what is being compared in Figures 2-4, rather than just showing the results.

In the revised manuscript we will add a visual aid for the three contrasts we consider.

We are happy to inform the editors that we have implemented, for the Reviewed Preprint, the direct textual Recommendations for the Authors given by Reviewers 2 and 3. We will implement the suggested Figure changes in our revised manuscript. We thank them for their feedback in strengthening our manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study develops and validates a neural subspace similarity analysis for testing whether neural representations of graph structures generalize across graph size and stimulus sets. The authors show the method works in rat grid and place cell data, finding that grid but not place cells generalize across different environments, as expected. The authors then perform additional analyses and simulations to show that this method should also work on fMRI data. Finally, the authors test their method on fMRI responses from the entorhinal cortex (EC) in a task that involves graphs that vary in size (and stimulus set) and statistical structure (hexagonal and community). They find neural representations of stimulus sets in lateral occipital complex (LOC) generalize across statistical structure and that EC activity generalizes across stimulus sets/graph size, but only for the hexagonal structures.

Strengths:

(1) The overall topic is very interesting and timely and the manuscript is well-written.

(2) The method is clever and powerful. It could be important for future research testing whether neural representations are aligned across problems with different state manifestations.

(3) The findings provide new insights into generalizable neural representations of abstract task states in the entorhinal cortex.

We thank the reviewer for their kind comments and clear summary of the paper and its strengths.

Weaknesses:

(1) The manuscript would benefit from improving the figures. Moreover, the clarity could be strengthened by including conceptual/schematic figures illustrating the logic and steps of the method early in the paper. This could be combined with an illustration of the remapping properties of grid and place cells and how the method captures these properties.

We agree with the reviewer and have added a schematic figure of the method (figure 1a).

(2) Hexagonal and community structures appear to be confounded by training order. All subjects learned the hexagonal graph always before the community graph. As such, any differences between the two graphs could thus be explained (in theory) by order effects (although this is practically unlikely). However, given community and hexagonal structures shared the same stimuli, it is possible that subjects had to find ways to represent the community structures separately from the hexagonal structures. This could potentially explain why the authors did not find generalizations across graph sizes for community structures.

We thank the reviewer for their comments. We agree that the null result regarding the community structures does not mean that EC doesn’t generalise over these structures, and that the training order could in theory contribute to the lack of an effect. The decision to keep the asymmetry of the training order was deliberate: we chose this order based on our previous study (Mark et al. 2020), where we show that learning a community structure first changes the learning strategy of subsequent graphs. We could have perhaps overcome this by increasing the training periods, but 1) the training period is already very long; 2) there will still be asymmetry because the group that first learn community structure will struggle in learning the hexagonal graph more than vice versa, as shown in Mark et al. 2020.

We have added the following sentences on this decision to the Methods section:

“We chose to first teach hexagonal graphs for all participants and not randomize the order because of previous results showing that first learning community structure changes participants’ learning strategy (mark et al. 2020).”

(3) The authors include the results from a searchlight analysis to show the specificity of the effects of EC. A better way to show specificity would be to test for a double dissociation between the visual and structural contrast in two independently defined regions (e.g., anatomical ROIs of LOC and EC).

Thanks for this suggestion. We indeed tried to run the analysis in a whole-ROI approach, but this did not result in a significant effect in EC. Importantly, we disagree with the reviewer that this is a “better way to show specificity” than the searchlight approach. In our view, the two analyses differ with respect to the spatial extent of the representation they test for. The searchlight approach is testing for a highly localised representation on the scale of small spheres with only 100 voxels. The signal of such a localised representation is likely to be drowned in the noise in an analysis that includes thousands of voxels which mostly don’t show the effect - as would be the case in the whole-ROI approach.

(4) Subjects had more experience with the hexagonal and community structures before and during fMRI scanning. This is another confound, and possible reason why there was no generalization across stimulus sets for the community structure.

See our response to comment (2).

Reviewer #2 (Public review):

Summary:

Mark and colleagues test the hypothesis that entorhinal cortical representations may contain abstract structural information that facilitates generalization across structurally similar contexts. To do so, they use a method called "subspace generalization" designed to measure abstraction of representations across different settings. The authors validate the method using hippocampal place cells and entorhinal grid cells recorded in a spatial task, then perform simulations that support that it might be useful in aggregated responses such as those measured with fMRI. Then the method is applied to fMRI data that required participants to learn relationships between images in one of two structural motifs (hexagonal grids versus community structure). They show that the BOLD signal within an entorhinal ROI shows increased measures of subspace generalization across different tasks with the same hexagonal structure (as compared to tasks with different structures) but that there was no evidence for the complementary result (ie. increased generalization across tasks that share community structure, as compared to those with different structures). Taken together, this manuscript describes and validates a method for identifying fMRI representations that generalize across conditions and applies it to reveal entorhinal representations that emerge across specific shared structural conditions.

Strengths:

I found this paper interesting both in terms of its methods and its motivating questions. The question asked is novel and the methods employed are new - and I believe this is the first time that they have been applied to fMRI data. I also found the iterative validation of the methodology to be interesting and important - showing persuasively that the method could detect a target representation - even in the face of a random combination of tuning and with the addition of noise, both being major hurdles to investigating representations using fMRI.

We thank the reviewer for their kind comments and the clear summary of our paper.

Weaknesses:

In part because of the thorough validation procedures, the paper came across to me as a bit of a hybrid between a methods paper and an empirical one. However, I have some concerns, both on the methods development/validation side, and on the empirical application side, which I believe limit what one can take away from the studies performed.

We thank the reviewer for the comment. We agree that the paper comes across as a bit of a methods-empirical hybrid. We chose to do this because we believe (as the reviewer also points out) that there is value in both aspects of the paper.

Regarding the methods side, while I can appreciate that the authors show how the subspace generalization method "could" identify representations of theoretical interest, I felt like there was a noticeable lack of characterization of the specificity of the method. Based on the main equation in the results section of the paper, it seems like the primary measure used here would be sensitive to overall firing rates/voxel activations, variance within specific neurons/voxels, and overall levels of correlation among neurons/voxels. While I believe that reasonable pre-processing strategies could deal with the first two potential issues, the third seems a bit more problematic - as obligate correlations among neurons/voxels surely exist in the brain and persist across context boundaries that are not achieving any sort of generalization (for example neurons that receive common input, or voxels that share spatial noise). The comparative approach (ie. computing difference in the measure across different comparison conditions) helps to mitigate this concern to some degree - but not completely - since if one of the conditions pushes activity into strongly spatially correlated dimensions, as would be expected if univariate activations were responsive to the conditions, then you'd expect generalization (driven by shared univariate activation of many voxels) to be specific to that set of conditions.

We thank the reviewer for their comments. We would like to point out that we demean each voxel within all states/piles (3-pictures sequences) in a given graph/task (what the reviewer is calling “a condition”). Hence there is no shared univariate activation of many voxels in response to a graph going into the computation, and no sensitivity to the overall firing rate/voxel activation.  Our calculation captures the variance across states conditions within a task (here a graph), over and above the univariate effect of graph activity. In addition, we spatially pre-whiten the data within each searchlight, meaning that noisy voxels with high noise variance will be downweighted and noise correlations between voxels are removed prior to applying our method.

A second issue in terms of the method is that there is no comparison to simpler available methods. For example, given the aims of the paper, and the introduction of the method, I would have expected the authors to take the Neuron-by-Neuron correlation matrices for two conditions of interest, and examine how similar they are to one another, for example by correlating their lower triangle elements. Presumably, this method would pick up on most of the same things - although it would notably avoid interpreting high overall correlations as "generalization" - and perhaps paint a clearer picture of exactly what aspects of correlation structure are shared. Would this method pick up on the same things shown here? Is there a reason to use one method over the other?

We thank the reviewer for this important and interesting point. We agree that calculating correlation between the upper triangular elements of the covariance or correlation matrices picks up similar, but not identical aspects of the data (see below the mathematical explanation that was added to the supplementary). When we repeated the searchlight analysis and calculated the correlation between the upper triangular entries of the Pearson correlation matrices we obtained an effect in the EC, though weaker than with our subspace generalization method (t=3.9, the effect did not survive multiple comparisons). Similar results were obtained with the correlation between the upper triangular elements of the covariance matrices(t=3.8, the effect did not survive multiple comparisons).

The difference between the two methods is twofold: 1) Our method is based on the covariance matrix and not the correlation matrix - i.e. a difference in normalisation. We realised that in the main text of the original paper we mistakenly wrote “correlation matrix” rather than “covariance matrix” (though our equations did correctly show the covariance matrix). We have corrected this mistake in the revised manuscript. 2) The weighting of the variance explained in the direction of each eigenvector is different between the methods, with some benefits of our method for identifying low-dimensional representations and for robustness to strong spatial correlations.  We have added a section “Subspace Generalisation vs correlating the Neuron-by-Neuron correlation matrices” to the supplementary information with a mathematical explanation of these differences.

Regarding the fMRI empirical results, I have several concerns, some of which relate to concerns with the method itself described above. First, the spatial correlation patterns in fMRI data tend to be broad and will differ across conditions depending on variability in univariate responses (ie. if a condition contains some trials that evoke large univariate activations and others that evoke small univariate activations in the region). Are the eigenvectors that are shared across conditions capturing spatial patterns in voxel activations? Or, related to another concern with the method, are they capturing changing correlations across the entire set of voxels going into the analysis? As you might expect if the dynamic range of activations in the region is larger in one condition than the other?

This is a searchlight analysis, therefore it captures the activity patterns within nearby voxels. Indeed, as we show in our simulation, areas with high activity and therefore high signal to noise will have better signal in our method as well. Note that this is true of most measures.

My second concern is, beyond the specificity of the results, they provide only modest evidence for the key claims in the paper. The authors show a statistically significant result in the Entorhinal Cortex in one out of two conditions that they hypothesized they would see it. However, the effect is not particularly large. There is currently no examination of what the actual eigenvectors that transfer are doing/look like/are representing, nor how the degree of subspace generalization in EC may relate to individual differences in behavior, making it hard to assess the functional role of the relationship. So, at the end of the day, while the methods developed are interesting and potentially useful, I found the contributions to our understanding of EC representations to be somewhat limited.

We agree with this point, yet believe that the results still shed light on EC functionality. Unfortunately, we could not find correlation between behavioral measures and the fMRI effect.

Reviewer #3 (Public review):

Summary:

The article explores the brain's ability to generalize information, with a specific focus on the entorhinal cortex (EC) and its role in learning and representing structural regularities that define relationships between entities in networks. The research provides empirical support for the longstanding theoretical and computational neuroscience hypothesis that the EC is crucial for structure generalization. It demonstrates that EC codes can generalize across non-spatial tasks that share common structural regularities, regardless of the similarity of sensory stimuli and network size.

Strengths:

(1) Empirical Support: The study provides strong empirical evidence for the theoretical and computational neuroscience argument about the EC's role in structure generalization.

(2) Novel Approach: The research uses an innovative methodology and applies the same methods to three independent data sets, enhancing the robustness and reliability of the findings.

(3) Controlled Analysis: The results are robust against well-controlled data and/or permutations.

(4) Generalizability: By integrating data from different sources, the study offers a comprehensive understanding of the EC's role, strengthening the overall evidence supporting structural generalization across different task environments.

Weaknesses:

A potential criticism might arise from the fact that the authors applied innovative methods originally used in animal electrophysiology data (Samborska et al., 2022) to noisy fMRI signals. While this is a valid point, it is noteworthy that the authors provide robust simulations suggesting that the generalization properties in EC representations can be detected even in low-resolution, noisy data under biologically plausible assumptions. I believe this is actually an advantage of the study, as it demonstrates the extent to which we can explore how the brain generalizes structural knowledge across different task environments in humans using fMRI. This is crucial for addressing the brain's ability in non-spatial abstract tasks, which are difficult to test in animal models.

While focusing on the role of the EC, this study does not extensively address whether other brain areas known to contain grid cells, such as the mPFC and PCC, also exhibit generalizable properties. Additionally, it remains unclear whether the EC encodes unique properties that differ from those of other systems. As the authors noted in the discussion, I believe this is an important question for future research.

We thank the reviewer for their comments. We agree with the reviewer that this is a very interesting question. We tried to look for effects in the mPFC, but we did not obtain results that were strong enough to report in the main manuscript, but we do report a small effect in the supplementary.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I wonder how important the PCA on B1(voxel-by-state matrix from environment 1) and the computation of the AUC (from the projection on B2 [voxel-by-state matrix from environment 1]) is for the analysis to work. Would you not get the same result if you correlated the voxel-by-voxel correlation matrix based on B1 (C1) with the voxel-by-voxel correlation matrix based on B2 (C2)? I understand that you would not have the subspace-by-subspace resolution that comes from the individual eigenvectors, but would the AUC not strongly correlate with the correlation between C1 and C2?

We agree with the reviewer comments - see our response to reviewer 2 second issue above. 

(2) There is a subtle difference between how the method is described for the neural recording and fMRI data. Line 695 states that principal components of the neuron x neuron intercorrelation matrix are computed, whereas line 888 implies that principal components of the data matrix B are computed. Of note, B is a voxel x pile rather than a pile x voxel matrix. Wouldn't this result in U being pile x pile rather than voxel x voxel?

The PCs are calculated on the neuron x neuron (or voxel x voxel) covariance matrix of the activation matrix. We’ve added the following clarification to the relevant part of the Methods:

“We calculated noise normalized GLM betas within each searchlight using the RSA toolbox. For each searchlight and each graph, we had a nVoxels (100) by nPiles (10) activation matrix (B) that describes the activation of a voxel as a result of a particular pile (three pictures’ sequence). We exploited the (voxel x voxel) covariance matrix of this matrix to quantify the manifold alignment within each searchlight.”

(3) It would be very helpful to the field if the authors would make the code and data publicly available. Please consider depositing the code for data analysis and simulations, as well as the preprocessed/extracted data for the key results (rat data/fMRI ROI data) into a publicly accessible repository.

The code is publicly available in git (https://github.com/ShirleyMgit/subspace_generalization_paper_code/tree/main).

(4) Line 219: "Kolmogorov Simonov test" should be "Kolmogorov Smirnov test".

thanks!

(5) Please put plots in Figure 3F on the same y-axis.

(6) Were large and small graphs of a given statistical structure learned on the same days, and if so, sequentially or simultaneously? This could be clarified.

The graphs are learned on the same day.  We clarified this in the Methods section.

Reviewer #2 (Recommendations for the authors):

Perhaps the advantage of the method described here is that you could narrow things down to the specific eigenvector that is doing the heavy lifting in terms of generalization... and then you could look at that eigenvector to see what aspect of the covariance structure persists across conditions of interest. For example, is it just the highest eigenvalue eigenvector that is likely picking up on correlations across the entire neural population? Or is there something more specific going on? One could start to get at this by looking at Figures 1A and 1C - for example, the primary difference for within/between condition generalization in 1C seems to emerge with the first component, and not much changes after that, perhaps suggesting that in this case, the analysis may be picking up on something like the overall level of correlations within different conditions, rather than a more specific pattern of correlations.

The nature of the analysis means the eigenvectors are organized by their contribution to the variance, therefore the first eigenvector is responsible for more variance than the other, we did not check rigorously whether the variance is then splitted equally by the remaining eigenvectors but it does not seems to be the case.

Why is variance explained above zero for fraction EVs = 0 for figure 1C (but not 1A) ? Is there some plotting convention that I'm missing here?

There was a small bug in this plot and it was corrected - thank you very much!

The authors say:

"Interestingly, the difference in AUCs was also 190 significantly smaller than chance for place cells (Figure 1a, compare dotted and solid green 191 lines, p<0.05 using permutation tests, see statistics and further examples in supplementary 192 material Figure S2), consistent with recent models predicting hippocampal remapping that is 193 not fully random (Whittington et al. 2020)."

But my read of the Whittington model is that it would predict slight positive relationships here, rather than the observed negative ones, akin to what one would expect if hippocampal neurons reflect a nonlinear summation of a broad swath of entorhinal inputs.

Smaller differences than chance imply that the remapping of place cells is not completely random.

Figure 2:

I didn't see any description of where noise amplitude values came from - or any justification at all in that section. Clearly, the amount of noise will be critical for putting limits on what can and cannot be detected with the method - I think this is worthy of characterization and explanation. In general, more information about the simulations is necessary to understand what was done in the pseudovoxel simulations. I get the gist of what was done, but these methods should clear enough that someone could repeat them, and they currently are not.

Thanks, we added noise amplitude to the figure legend and Methods.

What does flexible mean in the title? The analysis only worked for the hexagonal grid - doesn't that suggest that whatever representations are uncovered here are not flexible in the sense of being able to encode different things?

Flexible here means, flexible over stimulus’ characteristics that are not related to the structural form such as stimuli, the size of the graph etc.

Reviewer #3 (Recommendations for the authors):

I have noticed that the authors have updated the previous preprint version to include extensive simulations. I believe this addition helps address potential criticisms regarding the signal-to-noise ratio. If the authors could share the code for the fMRI data and the simulations in an open repository, it would enhance the study's impact by reaching a broader readership across various research fields. Except for that, I have nothing to ask for revision.

Thanks, the code will be publicly available: (https://github.com/ShirleyMgit/subspace_generalization_paper_code/tree/main).

Author response:

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

Reviewer #1 (Public review):

The authors present exciting new experimental data on the antigenic recognition of 78 H3N2 strains (from the beginning of the 2023 Northern Hemisphere season) against a set of 150 serum samples. The authors compare protection profiles of individual sera and find that the antigenic effect of amino acid substitutions at specific sites depends on the immune class of the sera, differentiating between children and adults. Person-to-person heterogeneity in the measured titers is strong, specifically in the group of children's sera. The authors find that the fraction of sera with low titers correlates with the inferred growth rate using maximum likelihood regression (MLR), a correlation that does not hold for pooled sera. The authors then measure the protection profile of the sera against historical vaccine strains and find that it can be explained by birth cohort for children. Finally, the authors present data comparing pre- and post- vaccination protection profiles for 39 (USA) and 8 (Australia) adults. The data shows a cohort-specific vaccination effect as measured by the average titer increase, and also a virus-specific vaccination effect for the historical vaccine strains. The generated data is shared by the authors and they also note that these methods can be applied to inform the bi-annual vaccine composition meetings, which could be highly valuable.

Thanks for this nice summary of our paper.

The following points could be addressed in a revision:

(1) The authors conclude that much of the person-to-person and strain-to-strain variation seems idiosyncratic to individual sera rather than age groups. This point is not yet fully convincing. While the mean titer of an individual may be idiosyncratic to the individual sera, the strain-to-strain variation still reveals some patterns that are consistent across individuals (the authors note the effects of substitutions at sites 145 and 275/276). A more detailed analysis, removing the individual-specific mean titer, could still show shared patterns in groups of individuals that are not necessarily defined by the birth cohort.

As the reviewer suggests, we normalized the titers for all sera to the geometric mean titer for each individual in the US-based pre-vaccination adults and children. This is only for the 2023-circulating viral strains. We then faceted these normalized titers by the same age groups we used in Figure 6, and the resulting plot is shown. Although there are differences among virus strains (some are better neutralized than others), there are not obvious age group-specific patterns (eg, the trends in the two facets are similar). This observation suggests that at least for these relatively closely related recent H3N2 strains, the strain-to-strain variation does not obviously segregate by age group. Obviously, it is possible (we think likely) that there would be more obvious age-group specific trends if we looked at a larger swath of viral strains covering a longer time range (eg, over decades of influenza evolution). We have added the new plots shown as a Supplemental Figure 6 in the revised manuscript.

(2) The authors show that the fraction of sera with a titer 138 correlates strongly with the inferred growth rate using MLR. However, the authors also note that there exists a strong correlation between the MLR growth rate and the number of HA1 mutations. This analysis does not yet show that the titers provide substantially more information about the evolutionary success. The actual relation between the measured titers and fitness is certainly more subtle than suggested by the correlation plot in Figure 5. For example, the clades A/Massachusetts and A/Sydney both have a positive fitness at the beginning of 2023, but A/Massachusetts has substantially higher relative fitness than A/Sydney. The growth inference in Figure 5b does not appear to map that difference, and the antigenic data would give the opposite ranking. Similarly, the clades A/Massachusetts and A/Ontario have both positive relative fitness, as correctly identified by the antigenic ranking, but at quite different times (i.e., in different contexts of competing clades). Other clades, like A/St. Petersburg are assigned high growth and high escape but remain at low frequency throughout. Some mention of these effects not mapped by the analysis may be appropriate.

Thanks for the nice summary of our findings in Figure 5. However, the reviewer is misreading the growth charts when they say that A/Massachusetts/18/2022 has a substantially higher fitness than A/Sydney/332/2023. Figure 5a (reprinted at left panel) shows the frequency trajectory of different variants over time. While A/Massachusetts/18/2022 reaches a higher frequency than A/Sydney/332/2023, the trajectory is similar and the reason that A/Massachusetts/18/2022 reached a higher max frequency is that it started at a higher frequency at the beginning of 2023. The MLR growth rate estimates differ from the maximum absolute frequency reached: instead, they reflect how rapidly each strain grows relative to others. In fact, A/Massachusetts/18/2022 and A/Sydney/332/2023 have similar growth rates, as shown in Supplemental Figure 6b (reprinted at right). Similarly, A/Saint-Petersburg/RII-166/2023 starts at a low initial frequency but then grows even as A/Massachusetts/18/2022 and A/Sydney/332/2023 are declining, and so has a higher growth rate than both of those. 

In the revised manuscript, we have clarified how viral growth rates are estimated from frequency trajectories, and how growth rate differs from max frequency in the text below:

“To estimate the evolutionary success of different human H3N2 influenza strains during 2023, we used multinomial logistic regression, which analyzes strain frequencies over time to calculate strain-specific relative growth rates [51–53]. There were sufficient sequencing counts to reliably estimate growth rates in 2023 for 12 of the HAs for which we measured titers using our sequencing-based neutralization assay libraries (Figure 5a,b and Supplemental Figure 9a,b). Note that these growth rates estimate how rapidly each strain grows relative to the other strains, rather than the absolute highest frequency reached by each strain “.  

(3) For the protection profile against the vaccine strains, the authors find for the adult cohort that the highest titer is always against the oldest vaccine strain tested, which is A/Texas/50/2012. However, the adult sera do not show an increase in titer towards older strains, but only a peak at A/Texas. Therefore, it could be that this is a virus-specific effect, rather than a property of the protection profile. Could the authors test with one older vaccine virus (A/Perth/16/2009?) whether this really can be a general property?

We are interested in studying immune imprinting more thoroughly using sequencing-based neutralization assays, but we note that the adults in the cohorts we studied would have been imprinted with much older strains than included in this library. As this paper focuses on the relative fitness of contemporary strains with minor secondary points regarding imprinting, these experiments are beyond the scope of this study. We’re excited for future work (from our group or others) to explore these points by making a new virus library with strains from multiple decades of influenza evolution. 

Reviewer #2 (Public review):

This is an excellent paper. The ability to measure the immune response to multiple viruses in parallel is a major advancement for the field, which will be relevant across pathogens (assuming the assay can be appropriately adapted). I only have a few comments, focused on maximising the information provided by the sera.

Thanks very much!

Firstly, one of the major findings is that there is wide heterogeneity in responses across individuals. However, we could expect that individuals' responses should be at least correlated across the viruses considered, especially when individuals are of a similar age. It would be interesting to quantify the correlation in responses as a function of the difference in ages between pairs of individuals. I am also left wondering what the potential drivers of the differences in responses are, with age being presumably key. It would be interesting to explore individual factors associated with responses to specific viruses (beyond simply comparing adults versus children).

We thank the reviewer for this interesting idea. We performed this analysis (and the related analyses described) and added this as a new Supplemental Figure 7, which is pasted after the response to the next related comment by the reviewer. 

For 2023-circulating strains, we observed basically no correlation between the strength of correlation between pairs of sera and the difference in age between those pairs of sera (Supplemental Figure 7), which was unsurprising given the high degree of heterogeneity between individual sera (Figure 3, Supplemental Figure 6, and Supplemental Figure 8). For vaccine strains, there is a moderate negative correlation only in the children, but not in the adults or the combined group of adults and children. This could be because the children are younger with limited and potentially more similar vaccine and exposure histories than the adults. It could also be because the children are overall closer in age than the adults.

Relatedly, is the phylogenetic distance between pairs of viruses associated with similarity in responses?

For 2023-circulating strains, across sera cohorts we observed a weak-to-moderate correlation between the strength of correlation between the neutralizing titers across all sera to pairs of viruses and the Hamming distances between virus pairs. For the same comparison with vaccine strains, we observed moderate correlations, but this must be caveated with the slightly larger range of Hamming distances between vaccine strains. Notably, many of the points on the negative correlation slope are a mix of egg- and cell-produced vaccine strains from similar years, but there are some strain comparisons where the same year’s egg- and cell-produced vaccine strains correlate poorly.

Figure 5C is also a really interesting result. To be able to predict growth rates based on titers in the sera is fascinating. As touched upon in the discussion, I suspect it is really dependent on the representativeness of the sera of the population (so, e.g., if only elderly individuals provided sera, it would be a different result than if only children provided samples). It may be interesting to compare different hypotheses - so e.g., see if a population-weighted titer is even better correlated with fitness - so the contribution from each individual's titer is linked to a number of individuals of that age in the population. Alternatively, maybe only the titers in younger individuals are most relevant to fitness, etc.

We’re very interested in these analyses, but suggest they may be better explored in subsequent works that could sample more children, teenagers and adults across age groups. Our sera set, as the reviewer suggests, may be under-powered to perform the proposed analysis on subsetted age groups of our larger age cohorts. 

In Figure 6, the authors lump together individuals within 10-year age categories - however, this is potentially throwing away the nuances of what is happening at individual ages, especially for the children, where the measured viruses cross different groups. I realise the numbers are small and the viruses only come from a small numbers of years, however, it may be preferable to order all the individuals by age (y-axis) and the viral responses in ascending order (x-axis) and plot the response as a heatmap. As currently plotted, it is difficult to compare across panels

This is a good suggestion. In the revised manuscript we have included a heatmap of the children and pre-vaccination adults, ordered by the year of birth of each individual, as Supplemental figure 8. That new figure is also pasted in this response.

Reviewer #3 (Public review):

The authors use high-throughput neutralisation data to explore how different summary statistics for population immune responses relate to strain success, as measured by growth rate during the 2023 season. The question of how serological measurements relate to epidemic growth is an important one, and I thought the authors present a thoughtful analysis tackling this question, with some clear figures. In particular, they found that stratifying the population based on the magnitude of their antibody titres correlates more with strain growth than using measurements derived from pooled serum data. However, there are some areas where I thought the work could be more strongly motivated and linked together. In particular, how the vaccine responses in US and Australia in Figures 6-7 relate to the earlier analysis around growth rates, and what we would expect the relationship between growth rate and population immunity to be based on epidemic theory.

Thank you for this nice summary. This reviewer also notes that the text related to figures 6 and 7 are more secondary to the main story presented in figures 3-5. The main motivation for including figures 6 and 7 were to demonstrate the wide-ranging applications of sequencing-based neutralization data. We have tried to clarify this with the following minor text revisions, which do not add new content but we hope smooth the transition between results sections. 

While the preceding analyses demonstrated the utility of sequencing-based neutralization assays for measuring titers of currently circulating strains, our library also included viruses with HAs from each of the H3N2 influenza Northern Hemisphere vaccine strains from the last decade (2014 to 2024, see Supplemental Table 1). These historical vaccine strains cover a much wider span of evolutionary diversity that the 2023-circulating strains analyzed in the preceding sections (Figure 2a,b and Supplemental Figure 2b-e). For this analysis, we focused on the cell-passaged strains for each vaccine, as these are more antigenically similar to their contemporary circulating strains than the egg-passaged vaccine strains since they lack the mutations that arise during growth of viruses in eggs [55–57] (Supplemental Table 1). 

Our sequencing-based assay could also be used to assess the impact of vaccination on neutralization titers against the full set of strains in our H3N2 library. To do this, we analyzed matched 28-day post-vaccination samples for each of the above-described 39 pre-vaccination samples from the cohort of adults based in the USA (Table 1). We also analyzed a smaller set of matched pre- and post-vaccination sera samples from a cohort of eight adults based in Australia (Table 1). Note that there are several differences between these cohorts: the USA-based cohort received the 2023-2024 Northern Hemisphere egg-grown vaccine whereas the Australia-based cohort received the 2024 Southern Hemisphere cell-grown vaccine, and most individuals in the USA-based cohort had also been vaccinated in the prior season whereas most individuals in the Australia-based cohort had not. Therefore, multiple factors could contribute to observed differences in vaccine response between the cohorts.

Reviewer #3 (Recommendations for the authors):

Main comments:

(1) The authors compare titres of the pooled sera with the median titres across individual sera, finding a weak correlation (Figure 4). I was therefore interested in the finding that geometric mean titre and median across a study population are well correlated with growth rate (Supplemental Figure 6c). It would be useful to have some more discussion on why estimates from a pool are so much worse than pooled estimates.

We thank this reviewer for this point. We would clarify that pooling sera is the equivalent of taking the arithmetic mean of the individual sera, rather than the geometric mean or median, which tends to bias the measurements of the pool to the outliers within the pool. To address this reviewer’s point, we’ve added the following text to the manuscript:

“To confirm that sera pools are not reflective of the full heterogeneity of their constituent sera, we created equal volume pools of the children and adult sera and measured the titers of these pools using the sequencing-based neutralization assay. As expected, neutralization titers of the pooled sera were always higher than the median across the individual constituent sera, and the pool titers against different viral strains were only modestly correlated with the median titers across individual sera (Figure 4). The differences in titers across strains were also compressed in the serum pools relative to the median across individual sera (Figure 4). The failure of the serum pools to capture the median titers of all the individual sera is especially dramatic for the children sera (Figure 4) because these sera are so heterogeneous in their individual titers (Figure 3b). Taken together, these results show that serum pools do not fully represent individual-level heterogeneity, and are similar to taking the arithmetic mean of the titers for a pool of individuals, which tends to be biased by the highest titer sera”.

(2) Perhaps I missed it, but are growth rates weekly growth rates? (I assume so?)

The growth rates are relative exponential growth rates calculated assuming a serial interval of 3.6 days. We also added clarifying language and a citation for the serial growth interval to the methods section:

The analysis performing H3 HA strain growth rate estimates using the evofr[51] package is at https://github.com/jbloomlab/flu_H3_2023_seqneut_vs_growth. Briefly, we sought to make growth rate estimates for the strains in 2023 since this was the same timeframe when the sera were collected. To achieve this, we downloaded all publicly-available H3N2 sequences from the GISAID[88] EpiFlu database, filtering to only those sequences that closely matched a library HA1 sequence (within one HA1 amino-acid mutation) and were collected between January 2023 and December 2023. If a sequence was within one HA1 amino-acid mutation of multiple library HA1 proteins then it was assigned to the closest one; if there were multiple equally close matches then it was assigned fractionally to each match. We only made growth rate estimates for library strains with at least 80 sequencing counts (Supplemental Figure 9a), and ignored counts for sequences that did not match a library strain (equivalent results were obtained if we instead fit a growth rate for these sequences as an “other” category). We then fit multinomial logistic regression models using the evofr[51] package assuming a serial interval of 3.6 days[101]  to the strain counts. For the plot in Figure 5a the frequencies are averaged over a 14-day sliding window for visual clarity, but the fits were to the raw sequencing counts. For most of the analyses in this paper we used models based on requiring 80 sequencing counts to make an estimate for strain growth rates, and counting a sequence as a match if it was within one amino-acid mutation; see https://jbloomlab.github.io/flu_H3_2023_seqneut_vs_growth/ for comparable analyses using different reasonable sequence count cutoffs (e.g., 60, 50, 40 and 30, as depicted in Supplemental Figure 9).  Across sequence cutoffs, we found that the fraction of individuals with low neutralization titers and number of HA1 mutations correlated strongly with these MLR-estimated strain growth rates.

(3)  I found Figure 3 useful in that it presents phylogenetic structure alongside titres, to make it clearer why certain clusters of strains have a lower response. In contrast, I found it harder to meaningfully interpret Figure 7a beyond the conclusion that vaccines lead to a fairly uniform rise in titre. Do the 275 or 276 mutations that seem important for adults in Figure 3 have any impact?

We are certainly interested in the questions this reviewer raises, and in trying to understand how well a seasonal vaccine protects against the most successful influenza variants that season. However, these post-vaccination sera were taken when neutralizing titers peak ~30 days after vaccination. Because of this, in the larger cohort of US-based post-vaccination adults, the median titers across sera to most strains appear uniformly high. In the Australian-based post-vaccination adults, there was some strain-to-strain variation in median titers across sera, but of course this must be caveated with the much smaller sample size. It might be more relevant to answer this question with longitudinally sampled sera, when titers begin to wane in the following months.

(4)  It could be useful to define a mechanistic relationship about how you would expect susceptibility (e.g. fraction with titre < X, where X is a good correlate) to relate to growth via the reproduction number: R = R0 x S. For example, under the assumption the generation interval G is the same for all, we have R = exp(r*G), which would make it possible to make a prediction about how much we would expect the growth rate to change between S = 0.45 and 0.6, as in Fig 5c. This sort of brief calculation (or at least some discussion) could add some more theoretical underpinning to the analysis, and help others build on the work in settings with different fractions with low titres. It would also provide some intuition into whether we would expect relationships to be linear.

This is an interesting idea for future work! However, the scope of our current study is to provide these experimental data and show a correlation with growth; we hope this can be used to build more mechanistic models in future.

(5) A key conclusion from the analysis is that the fraction above a threshold of ~140 is particularly informative for growth rate prediction, so would it be worth including this in Figure 6-7 to give a clearer indication of how much vaccination reduces contribution to strain growth among those who are vaccinated? This could also help link these figures more clearly with the main analysis and question.

Although our data do find ~140 to be the threshold that gives max correlation with growth rate, we are not comfortable strongly concluding 140 is a correlate of protection, as titers could influence viral fitness without completely protecting against infection. In addition, inspection of Figure 5d shows that while ~140 does give the maximal correlation, a good correlation is observed for most cutoffs in the range from ~40 to 200, so we are not sure how robustly we can be sure that ~140 is the optimal threshold.

(6)  In Figure 5, the caption doesn't seem to include a description for (e).

Thank you to the reviewer for catching this – this is fixed now.

(7)  The US vs Australia comparison could have benefited from more motivation. The authors conclude ,"Due to the multiple differences between cohorts we are unable to confidently ascribe a cause to these differences in magnitude of vaccine response" - given the small sample sizes, what hypotheses could have been tested with these data? The comparison isn't covered in the Discussion, so it seems a bit tangential currently.

Thank you to the reviewer for this comment, but we should clarify our aim was not to directly compare US and Australian adults. We are interested in regional comparisons between serum cohorts, but did not have the numbers to adequately address those questions here. This section (and the preceding question) were indeed both intended to be tangential to the main finding, and hopefully this will be clarified with our text additions in response to Reviewer #3’s public reviews.

Author response:

We thank the reviewers for their time and their constructive comments.

Reviewer 1 makes several incisive comments about the single-cell RNA-sequencing dataset used in this  version of the manuscript, which was previously published in Colquitt, 2021. The Reviewer correctly  notes that this dataset consists primarily of nuclei from zebra finches, with a relatively small proportion of  the data coming from Bengalese finches. However, all other data presented here comes from assays and  experiments in Bengalese finches. This discrepancy could lead to two issues of interpretation. First, there  could be substantive expression differences in the CRH signaling pathway between these two species,  making it difficult to interpret its cellular expression profile. Second, the Reviewer describes that in their  reanalysis of this dataset they determined that what had been described as distinct cell types – namely  HVC-Glut-1 vs. HVC-Glut-4 (corresponding to the HVC  RA  projection neurons) and the three RA-Glut  types – are likely to be single cell types. The Reviewer notes that inter-individual differences in gene  expression, which were not analyzed in the original publication, could have generated this apparent cell  type diversity.

To the first point, we agree that the use of the published dataset that consists primarily of zebra finch  data is not ideal when making claims of cell type-specific expression in Bengalese finches. To rectify this  issue, we have generated additional sets of snRNA-seq from Bengalese finches that encompass multiple  areas of the song system as well as adjacent comparator regions outside of the principal song areas.  Our initial analysis of these datasets indicates that the cellular patterns of expression of the CRH system  is consistent with what has been presented here. In our revision, we will include a reanalysis of  neuropeptide expression using these more extensive datasets.

To the second point, we also agree that some of the instances of glutamatergic neuron diversity could  have been generated either by issues stemming from the integration of two species or through  interindividual differences. In our analysis of our newer snRNA-seq data, we also identify a single HVC  RA  projection neuron type (not two) and that RA projection neuron types fall into one or two classes (not  three), similar to what Reviewer 1 described. We have deconvolved these datasets by genotype, as  suggested by the Reviewer, and do not see substantial interindividual variation across the CRH system.  However, our revision will explicitly address these issues.

Reviewer 1 also brings up several important questions concerning the relationships between CRHBP  and singing and the challenge of interpreting the influences of song acquisition and deafening on CRHBP  expression, given the variation in singing that generally accompanies these changes to song. To address  in part this issue, our regression analysis of deafening-associated gene expression differences includes  a term for the number of songs sung on the day of euthanasia as well as an interaction term between  song destabilization and singing amount. This design controls for the amount that a bird sang in the  period before brain collection. This analysis was included in  (Colquitt et al., 2023) , and will be further  elaborated and discussed in the revised version of this manuscript. Notably, CRHBP expression shows a  significant interaction between song destabilization and singing amount, suggesting that reduction of  CRHBP following deafening is greater than what would be expected from any reductions in singing  alone. This specific analysis will be included in the revised manuscript as well.

However, despite these statistical controls, we cannot fully rule out that singing is playing a fundamental  role in driving the CRHBP expression differences we see across conditions. Indeed, a number of studies  have described an association between the amount a bird sings and the variability of its song  (Chen et  al., 2013; Hayase et al., 2018; Hilliard et al., 2012; Miller et al., 2010; Ohgushi et al., 2015) , with a general trend of higher amounts of singing correlated with a reduction in variability. This relationship is  consistent with what we see for CRHBP expression in RA and HVC: high in unmanipulated adult males  and decreased during states of high variability and plasticity (post-deafening and juveniles). A model that  combines these observations, and that we will include in the Discussion of the revised manuscript, is one  in which singing induces the expression of CRHBP in RA and HVC, limiting CRH binding to its receptors,  thereby limiting this pathway’s proposed effects on the excitability and synaptic plasticity of projection  neurons.

Reviewer 2 suggests multiple interesting avenues to more fully characterize the role of the CRH pathway  in song performance and learning. First, we agree that HVC is a compelling target to investigate CRH’s  role in song, given the similarity of CRHBP expression in HVC and RA across deafening, song  acquisition, and singing. As the Reviewer notes, a number of studies have demonstrated key roles for  interneurons in shaping neuronal dynamics in HVC and regulating song structure. Here, we focused on  RA due to the direct influence of RA projection neurons have on syringeal and respiration motoneurons  controlling song production, and the following expectation that manipulations of CRH signaling in this  region would have particularly measurable effects on song.  However, we agree with the reviewer that it  would be of additional interest to investigate manipulations of CRH signalling in HVC.  We are  considering whether it will be feasible given the usual constraints of time, personnel, and other  competing demands to carry such experiments as an addition to the current manuscript. Depending on  how that goes, we will either add new experimental data to the manuscript, or simply acknowledge the  interest of such experiments in Discussion and defer their pursuit to future study.

Likewise, Reviewer 2 suggests other ways in which an understanding of the role of CRH signalling could  be further enriched with additional experiments, including investigating the influence of CRH signaling on  song acquisition, when song transitions from a variable and plastic state to a precise and stereotyping  state, and pursuing direct evidence that CRH influences the neurophysiology of glutamatergic neurons in  HVC or RA. These are both excellent suggestions for ways in neuropeptide signalling could be further  linked to alterations in behavior; As we proceed with revisions we will consider whether we can address  some of these suggestions within the scope of the current manuscript, versus note them in discussion as  directions for future research.

Chen Q, Heston JB, Burkett ZD, White SA. 2013. Expression analysis of the speech-related genes  FoxP1 and FoxP2 and their relation to singing behavior in two songbird species.  J Exp Biol  216 :3682–3692. doi:10.1242/jeb.085886

Colquitt BM, Li K, Green F, Veline R, Brainard MS. 2023. Neural circuit-wide analysis of changes to gene  expression during deafening-induced birdsong destabilization.  Elife  12 :e85970. doi:10.7554/eLife.85970

Hayase S, Wang H, Ohgushi E, Kobayashi M, Mori C, Horita H, Mineta K, Liu W-C, Wada K. 2018. Vocal  practice regulates singing activity-dependent genes underlying age-independent vocal learning in  songbirds.  PLoS Biol 16 :e2006537. doi:10.1371/journal.pbio.2006537

Hilliard AT, Miller JE, Fraley ER, Horvath S, White SA. 2012. Molecular microcircuitry underlies functional  specification in a basal ganglia circuit dedicated to vocal learning.  Neuron  73 :537–552.  doi:10.1016/j.neuron.2012.01.005

Miller JE, Hilliard AT, White SA. 2010. Song practice promotes acute vocal variability at a key stage of  sensorimotor learning.  PLoS One  5 :e8592. doi:10.1371/journal.pone.0008592

Ohgushi E, Mori C, Wada K. 2015. Diurnal oscillation of vocal development associated with clustered  singing by juvenile songbirds.  J Exp Biol  218 :2260–2268.  doi:10.1242/jeb.115105

Author response:

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

Reviewer #1 (Public Review):

This study presents an exploration of PPGL tumour bulk transcriptomics and identifies three clusters of samples (labeled as subtypes C1-C3). Each subtype is then investigated for the presence of somatic mutations, metabolism-associated pathways and inflammation correlates, and disease progression. The proposed subtype descriptions are presented as an exploratory study. The proposed potential biomarkers from this subtype are suitably caveated and will require further validation in PPGL cohorts together with a mechanistic study.  

The first section uses WGCNA (a method to identify clusters of samples based on gene expression correlations) to discover three transcriptome-based clusters of PPGL tumours. The second section inspects a previously published snRNAseq dataset, and labels some of the published cells as subtypes C1, C2, C3 (Methods could be clarified here), among other cells labelled as immune cell types. Further details about how the previously reported single-nuclei were assigned to the newly described subtypes C1-C3 require clarification.

Thank you for your valuable suggestion. In response to the reviewer’s request for further clarification on “how previously published single-nuclei data were assigned to the newly defined C1-C3 subtypes,” we have provided additional methodological details in the revised manuscript (lines 103-109). Specifically, we aggregated the single-nucleus RNA-seq data to the sample level by summing gene counts across nuclei to generate pseudo-bulk expression profiles. These profiles were then normalized for library size, log-transformed (log1p), and z-scaled across samples. Using genesets scores derived from our earlier WGCNA analysis of PPGLs, we defined transcriptional subtypes within the Magnus cohort (Supplementary Figure. 1C). We further analyzed the single-nucleus data by classifying malignant (chromaffin) nuclei as C1, C2, or C3 based on their subtype scores, while non-malignant nuclei (including immune, stromal, endothelial, and others) were annotated using canonical cell-type markers (Figure. 4A). 

The tumour samples are obtained from multiple locations in the body (Figure 1A). It will be important to see further investigation of how the sample origin is distributed among the C1C3 clusters, and whether there is a sample-origin association with mutational drivers and disease progression.

Thank you for your valuable suggestion. In the revised manuscript (lines 74-79), Figure. 1A, Table S1 and Supplementary Figure. 1A, we harmonized anatomic site annotations from our PPGL cohort and the TCGA cohort and analyzed the distribution of tumor origin (adrenal vs extra-adrenal) across subtypes. The site composition is essentially uniform across C1-C3— approximately 75% pheochromocytoma (PC) and 25% paraganglioma (PG)—with only minimal variation. Notably, the proportion of extra-adrenal origin (paraganglioma origin) is slightly higher in the C1 subtype (see Supplementary Figure 1A), which aligns with the biological characteristics of tumors from this anatomical site, which typically exhibit more aggressive behavior.

Reviewer #2 (Public Review):

A study that furthers the molecular definition of PPGL (where prognosis is variable) and provides a wide range of sub-experiments to back up the findings. One of the key premises of the study is that identification of driver mutations in PPGL is incomplete and that compromises characterisation for prognostic purposes. This is a reasonable starting point on which to base some characterisation based on different methods. The cohort is a reasonable size, and a useful validation cohort in the form of TCGA is used. Whilst it would be resource-intensive (though plausible given the rarity of the tumour type) to perform RNA-seq on all PPGL samples in clinical practice, some potential proxies are proposed.

We sincerely thank the reviewer for their positive assessment of our study’s rationale. We fully agree that RNA sequencing for all PPGL samples remains resource-intensive in current clinical practice, and its widespread application still faces feasibility challenges. It is precisely for this reason that, after defining transcriptional subtypes, we further focused on identifying and validating practical molecular markers and exploring their detectability at the protein level.

In this study, we validated key markers such as ANGPT2, PCSK1N, and GPX3 using immunohistochemistry (IHC), demonstrating their ability to effectively distinguish among molecular subtypes (see Figure. 5). This provides a potential tool for the clinical translation of transcriptional subtyping, similar to the transcription factor-based subtyping in small cell lung cancer where IHC enables low-cost and rapid molecular classification.

It should be noted that the subtyping performance of these markers has so far been preliminarily validated only in our internal cohort of 87 PPGL samples. We agree with the reviewer that largerscale, multi-center prospective studies are needed in the future to further establish the reliability and prognostic value of these markers in clinical practice.

The performance of some of the proxy markers for transcriptional subtype is not presented.

We agree with your comment regarding the need to further evaluate the performance of proxy markers for transcriptional subtyping. In our study, we have in fact taken this point into full consideration. To translate the transcriptional subtypes into a clinically applicable classification tool, we employed a linear regression model to compare the effect values (β values) of candidate marker genes across subtypes (Supplementary Figure. 1D-F). Genes with the most significant β values and statistical differences were selected as representative markers for each subtype.

Ultimately, we identified ANGPT2, PCSK1N, and GPX3—each significantly overexpressed in subtypes C1, C2, and C3, respectively, and exhibiting the most pronounced β values—as robust marker genes for these subtypes (Figure. 5A and Supplementary Figure. 1D-F). These results support the utility of these markers in subtype classification and have been thoroughly validated in our analysis.

There is limited prognostic information available.

Thank you for your valuable suggestion. In this exploratory revision, we present the available prognostic signal in Figure. 5C. Given the current event numbers and follow-up time, we intentionally limited inference. We are continuing longitudinal follow-up of the PPGL cohort and will periodically update and report mature time-to-event analyses in subsequent work.

Reviewer #1 (Recommendations for the authors):

There is no deposition reference for the RNAseq transcriptomics data. Have the data been deposited in a suitable data repository?

Thank you for your valuable suggestion. We have updated the Data availability section (lines 508–511) to clarify that the bulk-tissue RNA-seq datasets generated in this study are available from the corresponding author upon reasonable request.

In the snRNAseq analysis of existing published data, clarify how cells were labelled as "C1", "C2", "C3", alongside cells labelled by cell type (the latter is described briefly in the Methods).

Thank you for your valuable suggestion. In response to the reviewer’s request for further clarification on “how previously published single-nuclei data were assigned to the newly defined C1-C3 subtypes,” we have provided additional methodological details in the revised manuscript (lines 103-109). Specifically, we aggregated the single-nucleus RNA-seq data to the sample level by summing gene counts across nuclei to generate pseudo-bulk expression profiles. These profiles were then normalized for library size, log-transformed (log1p), and z-scaled across samples. Using genesets scores derived from our earlier WGCNA analysis of PPGLs, we defined transcriptional subtypes within the Magnus cohort (Supplementary Figure. 1C). We further analyzed the single-nucleus data by classifying malignant (chromaffin) nuclei as C1, C2, or C3 based on their subtype scores, while non-malignant nuclei (including immune, stromal, endothelial, and others) were annotated using canonical cell-type markers (Figure. 4A).

Package versions should be included (e.g., CellChat, monocle2).

We greatly appreciate your comments and have now added a dedicated “Software and versions” subsection in Methods. Specifically, we report Seurat (v4.4.0), sctransform (v0.4.2), CellChat (v2.2.0), monocle (v2.36.0; monocle2), pheatmap (v1.0.13), clusterProfiler (v4.16.0), survival (v3.8.3), and ggplot2 (v3.5.2) (lines 514-516). We also corrected a typographical error (“mafools” → “maftools”) (lines 463).

Reviewer #2 (Recommendations for the authors):

It would be helpful to provide a little more detail on the clinical composition of the cohort (e.g., phaeo vs paraganglioma, age, etc.) in the text, acknowledging that this is done in Figure 1.

Thank you for your valuable suggestion. In the revision, we added Table S1 that provides a detailed summary of the clinical composition of the PPGL cohort. Specifically, we report the numbers and proportions (Supplementary Figure. 1A) of pheochromocytoma (PC) versus paraganglioma (PG), further subclassifying PG into head and neck (HN-PG), retroperitoneal (RPPG), and bladder (BC-PG).

How many of each transcriptional subtype had driver mutations (germline or somatic)? This is included in the figures but would be worth mentioning in the text. Presumably, some of these may be present but not detected (e.g., non-coding variants), and this should be commented on. It is feasible that if methods to detect all the relevant genomic markers were improved, then the rate of tumours without driver mutations would be less and their prognostic utility would be more comprehensive.

Thank you for your valuable suggestion. In the revision (lines 113–116), we now report the prevalence of driver mutations (germline or somatic) overall and by transcriptional subtype. We analyzed variant data across 84 PPGL-relevant genes from 179 tumors in the TCGA cohort and 30 tumors in Magnus’s cohort (Fig. 2A; Table S2). High-frequency genes were consistent with known biology—C1 enriched for [e.g., VHL/SDHB], C2 for [e.g., RET/HRAS], and C3 for [e.g., SDHA/SDHD]. We also note that a subset of tumors lacked an identifiable driver, which likely reflects current assay limitations (e.g., non-coding or structural variants, subclonality, and purity effects). Broader genomic profiling (deep WGS/long-read, RNA fusion, methylation) would be expected to reduce the “driver-negative” fraction and further enhance the prognostic utility of these classifiers.

ANGPT2 provides a reasonable predictive capacity for the C1 subtype as defined by the ROC AUC. What was the performance of the PCSK1N and GPX3 as markers of the other subtypes?

We agree with your comment regarding the need to further evaluate the performance of proxy markers for transcriptional subtyping, and we have supplemented the analysis with ROC and AUC values for two additional parameters (Author response image 1 , see below). Furthermore, in our study, we have in fact taken this point into full consideration. To translate the transcriptional subtypes into a clinically applicable classification tool, we employed a linear regression model to compare the effect values (β values) of candidate marker genes across subtypes (Supplementary Figure. 1D-F). Genes with the most significant β values and statistical differences were selected as representative markers for each subtype.

Ultimately, we identified ANGPT2, PCSK1N, and GPX3—each significantly overexpressed in subtypes C1, C2, and C3, respectively, and exhibiting the most pronounced β values—as robust marker genes for these subtypes (Figure. 5A and Supplementary Figure. 1D-F). These results support the utility of these markers in subtype classification and have been thoroughly validated in our analysis.

Author response image 1.

Extended Data Figure A-B. (A) The ROC curve illustrates the diagnostic ability to distinguish PCSK1N expression in PPGLs, specifically differentiating subtype C2 from non-C2 subtypes. The red dot indicates the point with the highest sensitivity (93.1%) and specificity (82.8%). AUC, the area under the curve. (B) The ROC curve illustrates the diagnostic ability to distinguish GPX3 expression in PPGLs, specifically differentiating subtype C3 from non-C3 subtypes. The red dot indicates the point with the highest sensitivity (83.0%) and specificity (58.8%). AUC, the area under the curve.

In the discussion, I think it would be valuable to summarise existing clinical/molecular predictors in PPGL and, acknowledging that their performance may be limited, compare them to the potential of these novel classifiers.

Thank you for your valuable suggestion. We have added a concise overview of established clinical and molecular predictors in PPGL and compared them with the potential of our transcriptional classifiers. The new paragraph (Discussion, lines 315–338) now reads:

“Compared to existing clinical and molecular predictors, risk assessment in PPGL has long relied on the following indicators: clinicopathological features (e.g., tumor size, non-adrenal origin, specific secretory phenotype, Ki-67 index), histopathological scoring systems (such as PASS/GAPP), and certain genetic alterations (including high-risk markers like SDHB inactivation mutations, as well as susceptibility gene mutations in ATRX, TERT promoter, MAML3, VHL, NF1, among others). Although these metrics are highly actionable in clinical practice, they exhibit several limitations: first, current molecular markers only cover a subset of patients, and technical constraints hinder the detection of many potentially significant variants (e.g., non-coding mutations), thereby compromising the comprehensiveness of prognostic evaluation; second, histopathological scoring is susceptible to interobserver variability; furthermore, the lack of standardized detection and evaluation protocols across institutions limits the comparability and generalizability of results. Our transcriptomic classification system—comprising C1 (pseudohypoxic/angiogenic signature), C2 (kinase-signaling signature), and C3 (SDHx-related signature)—provides a complementary approach to PPGL risk assessment. These subtypes reflect distinct biological backgrounds tied to specific genetic alterations and can be approximated by measuring the expression of individual genes (e.g., ANGPT2, PCSK1N, or GPX3). This study demonstrates that the classifier offers three major advantages: first, it accurately distinguishes subtypes with coherent biological features; second, it retains significant predictive value even after adjusting for clinical covariates; third, it can be implemented using readily available assays such as immunohistochemistry. These findings suggest that integrating transcriptomic subtyping with conventional clinical markers may offer a more comprehensive and generalizable risk stratification framework. However, this strategy would require validation through multi-center prospective studies and standardization of detection protocols.”

A little more explanation of the principles behind WGCNA would be useful in the methods.

We are grateful for your comments. We have expanded the Methods to briefly explain the principles of WGCNA (lines 426-454). In short, WGCNA constructs a weighted coexpression network from normalized gene expression, identifies modules of tightly co-expressed genes, summarizes each module by its eigengene (the first principal component), and then correlates module eigengenes with phenotypes (e.g., transcriptional subtypes) to highlight biologically meaningful gene sets and candidate hub genes. We now specify our preprocessing, choice of softthresholding power to approximate scale-free topology, module detection/merging criteria, and the statistics used for module–trait association and downstream gene-set scoring. 

On line 234, I think the figure should be 5C?

We greatly appreciate your comments and Correct to Figure 5C.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Weakness:

I wonder how task difficulty and linguistic labels interact with the current findings. Based on the behavioral data, shapes with more geometric regularities are easier to detect when surrounded by other shapes. Do shape labels that are readily available (e.g., "square") help in making accurate and speedy decisions? Can the sensitivity to geometric regularity in intraparietal and inferior temporal regions be attributed to differences in task difficulty? Similarly, are the MEG oddball detection effects that are modulated by geometric regularity also affected by task difficulty?

We see two aspects to the reviewer’s remarks.

(1) Names for shapes.

On the one hand, is the question of the impact of whether certain shapes have names and others do not in our task. The work presented here is not designed to specifically test the effect of formal western education; however, in previous work (Sablé-Meyer et al., 2021), we noted that the geometric regularity effect remains present even for shapes that do not have specific names, and even in participants who do not have names for them. Thus, we replicated our main effects with both preschoolers and adults that did not attend formal western education and found that our geometric feature model remained predictive of their behavior; we refer the reader to this previous paper for an extensive discussion of the possible role of linguistic labels, and the impact of the statistics of the environment on task performance.  

What is more, in our behavior experiments we can discard data from any shape that is has a name in English and run our model comparison again. Doing so diminished the effect size of the geometric feature model, but it remained predictive of human behavior: indeed, if we removed all shapes but kite, rightKite, rustedHinge, hinge and random (i.e., more than half of our data, and shapes for which we came up with names but there are no established names), we nevertheless find that both models significantly correlate with human behavior—see plot in Author response image 1, equivalent of our Fig. 1E with the remaining shapes.

Author response image 1.

An identical analysis on the MEG leads to two noisy but significant clusters (CNN: 64.0ms to 172.0ms; then 192.0ms to 296.0ms; both p<.001: Geometric Features: 312.0ms to 364.0ms with p=.008). We have improved our manuscript thanks to the reviewer’s observation by adding a figure with the new behavior analysis to the supplementary figures and in the result section of the behavior task. We now refer to these analysis where appropriate:

(intro) “The effect appeared as a human universal, present in preschoolers, first-graders, and adults without access to formal western math education (the Himba from Namibia), and thus seemingly independent of education and of the existence of linguistic labels for regular shapes.”

(behavior results) “Finally, to separate the effect of name availability and geometric features on behavior, we replicated our analysis after removing the square, rectangle, trapezoids, rhombus and parallelogram from our data (Fig. S5D). This left us with five shapes, and an RDM with 10 entries, When regressing it in a GLM with our two models, we find that both models are still significant predictors (p<.001). The effect size of the geometric feature model is greatly reduced, yet remained significantly higher than that of the neural network model (p<.001).”

(meg results) “This analysis yielded similar clusters when performed on a subset of shapes that do not have an obvious name in English, as was the case for the behavior analysis (CNN Encoding: 64.0ms to 172.0ms; then 192.0ms to 296.0ms; both p<.001: Geometric Features: 312.0ms to 364.0ms with p=.008).”

(discussion, end of behavior section) “Previously, we only found such a significant mixture of predictors in uneducated humans (whether French preschoolers or adults from the Himba community, mitigating the possible impact of explicit western education, linguistic labels, and statistics of the environment on geometric shape representation) (Sablé-Meyer et al., 2021).”

Perhaps the referee’s point can also be reversed: we provide a normative theory of geometric shape complexity which has the potential to explain why certain shapes have names: instead of seeing shape names as the cause of their simpler mental representation, we suggest that the converse could occur, i.e. the simpler shapes are the ones that are given names.

(2) Task difficulty

On the other hand is the question of whether our effect is driven by task difficulty. First, we would like to point out that this point could apply to the fMRI task, which asks for an explicit detection of deviants, but does not apply to the MEG experiment. In MEG, participants passively looked at sequences of shapes which, for a given block, comprising many instances of a fixed standard shape and rare deviants–even if they notice deviants, they have no task related to them. Yet two independent findings validated the geometric features model: there was a large effect of geometric regularity on the MEG response to deviants, and the MEG dissimilarity matrix between standard shapes correlated with a model based on geometric features, better than with a model based on CNNs. While the response to rare deviants might perhaps be attributed to “difficulty” (assuming that, in spite of the absence of an explicit task, participants try to spot the deviants and find this self-imposed task more difficult in runs with less regular shapes), it seems very hard to explain the representational similarity analysis (RSA) findings based on difficulty. Indeed, what motivated us to use RSA analysis in both fMRI and MEG was to stop relying on the response to deviants, and use solely the data from standard or “reference” shapes, and model their neural response with theory-derived regressors.

We have updated the manuscript in several places to make our view on these points clearer:

(experiment 4) “This design allowed us to study the neural mechanisms of the geometric regularity effect without confounding effects of task, task difficulty, or eye movements.”

(figure 4, legend) “(A) Task structure: participants passively watch a constant stream of geometric shapes, one per second (presentation time 800ms). The stimuli are presented in blocks of 30 identical shapes up to scaling and rotation, with 4 occasional deviant shape. Participants do not have a task to perform beside fixating.”

Reviewer #2 (Public review):

Weakness:

Given that the primary take away from this study is that geometric shape information is found in the dorsal stream, rather than the ventral stream there is very little there is very little discussion of prior work in this area (for reviews, see Freud et al., 2016; Orban, 2011; Xu, 2018). Indeed, there is extensive evidence of shape processing in the dorsal pathway in human adults (Freud, Culham, et al., 2017; Konen & Kastner, 2008; Romei et al., 2011), children (Freud et al., 2019), patients (Freud, Ganel, et al., 2017), and monkeys (Janssen et al., 2008; Sereno & Maunsell, 1998; Van Dromme et al., 2016), as well as the similarity between models and dorsal shape representations (Ayzenberg & Behrmann, 2022; Han & Sereno, 2022).

We thank the reviewer for this opportunity to clarify our writing. We want to use this opportunity to highlight that our primary finding is not about whether the shapes of objects or animals (in general) are processed in the ventral versus or the dorsal pathway, but rather about the much more restricted domain of geometric shapes such as squares and triangles. We propose that simple geometric shapes afford additional levels of mental representation that rely on their geometric features – on top of the typical visual processing. To the best of our knowledge, this point has not been made in the above papers.

Still, we agree that it is useful to better link our proposal to previous ones. We have updated the discussion section titled “Two Visual Pathways” to include more specific references to the literature that have reported visual object representations in the dorsal pathway. Following another reviewer’s observation, we have also updated our analysis to better demonstrate the overlap in activation evoked by math and by geometry in the IPS, as well as include a novel comparison with independently published results.

Overall, to address this point, we (i) show the overlap between our “geometry” contrast (shape > word+tools+houses) and our “math” contrast (number > words); (ii) we display these ROIs side by side with ROIs found in previous work (Amalric and Dehaene, 2016), and (iii) in each math-related ROIs reported in that article, we test our “geometry” (shape > word+tools+houses) contrast and find almost all of them to be significant in both population; see Fig. S5.

Finally, within the ROIs identified with our geometry localizer, we also performed similarity analyses: for each region we extracted the betas of every voxel for every visual category, and estimated the distance (cross-validated mahalanobis) between different visual categories. In both ventral ROIs, in both populations, numbers were closer to shapes than to the other visual categories including text and Chinese characters (all p<.001). In adults, this result also holds for the right ITG (p=.021) and the left IPS (p=.014) but not the right IPS (p=.17). In children, this result did not hold in the areas.

Naturally, overlap in brain activation does not suffice to conclude that the same computational processes are involved. We have added an explicit caveat about this point. Indeed, throughout the article,  we have been careful to frame our results in a way that is appropriate given our evidence, e.g. saying “Those areas are similar to those active during number perception, arithmetic, geometric sequences, and the processing of high-level math concepts” and “The IPS areas activated by geometric shapes overlap with those active during the comprehension of elementary as well as advanced mathematical concepts”. We have rephrased the possibly ambiguous “geometric shapes activated math- and number-related areas, particular the right aIPS.” into “geometric shapes activated areas independently found to be activated by math- and number-related tasks, in particular the right aIPS”.

Reviewer #3 (Public review):

Weakness:

Perhaps the manuscript could emphasize that the areas recruited by geometric figures but not objects are spatial, with reduced processing in visual areas. It also seems important to say that the images of real objects are interpreted as representations of 3D objects, as they activate the same visual areas as real objects. By contrast, the images of geometric forms are not interpreted as representations of real objects but rather perhaps as 2D abstractions.

This is an interesting possibility. Geometric shapes are likely to draw attention to spatial dimensions (e.g. length) and to do so in a 2D spatial frame of reference rather than the 3D representations evoked by most other objects or images. However, this possibility would require further work to be thoroughly evaluated, for instance by comparing usual 3D objects with rare instances of 2D ones (e.g. a sheet of paper, a sticker etc). In the absence of such a test, we refrained from further speculation on this point.

The authors use the term "symbolic." That use of that term could usefully be expanded here.  

The reviewer is right in pointing out that “symbolic” should have been more clearly defined. We now added in the introduction:

(introduction) “[…] we sometimes refer to this model as “symbolic” because it relies on discrete, exact, rule-based features rather than continuous representations  (Sablé-Meyer et al., 2022). In this representational format, geometric shapes are postulated to be represented by symbolic expressions in a “language-of-thought”, e.g. “a square is a four-sided figure with four equal sides and four right angles” or equivalently by a computer-like program from drawing them in a Logo-like language (Sablé-Meyer et al., 2022).”

Here, however, the present experiments do not directly probe this format of a representation. We have therefore simplified our wording and removed many of our use of the word “symbolic” in favor of the more specific “geometric features”.

Pigeons have remarkable visual systems. According to my fallible memory, Herrnstein investigated visual categories in pigeons. They can recognize individual people from fragments of photos, among other feats. I believe pigeons failed at geometric figures and also at cartoon drawings of things they could recognize in photos. This suggests they did not interpret line drawings of objects as representations of objects.

The comparison of geometric abilities across species is an interesting line of research. In the discussion, we briefly mention several lines of research that indicate that non-human primates do not perceive geometric shapes in the same way as we do – but for space reasons, we are reluctant to expand this section to a broader review of other more distant species. The referee is right that there is evidence of pigeons being able to perceive an invariant abstract 3D geometric shape in spite of much variation in viewpoint (Peissig et al., 2019) – but there does not seem to be evidence that they attend to geometric regularities specifically (e.g. squares versus non-squares). Also, the referee’s point bears on the somewhat different issue of whether humans and other animals may recognize the object depicted by a symbolic drawing (e.g. a sketch of a tree). Again, humans seem to be vastly superior in this domain, and research on this topic is currently ongoing in the lab. However, the point that we are making in the present work is specifically about the neural correlates of the representation of simple geometric shapes which by design were not intended to be interpretable as representations of objects.

Categories are established in part by contrast categories; are quadrilaterals, triangles, and circles different categories?

We are not sure how to interpret the referee’s question, since it bears on the definition of “category” (Spontaneous? After training? With what criterion?). While we are not aware of data that can unambiguously answer the reviewer’s question, categorical perception in geometric shapes can be inferred from early work investigating pop-out effects in visual search, e.g. (Treisman and Gormican, 1988): curvature appears to generate strong pop-out effects, and therefore we would expect e.g. circles to indeed be a different category than, say, triangles. Similarly, right angles, as well as parallel lines, have been found to be perceived categorically (Dillon et al., 2019).

This suggests that indeed squares would be perceived as categorically different from triangles and circles. On the other hand, in our own previous work (Sablé-Meyer et al., 2021) we have found that the deviants that we generated from our quadrilaterals did not pop out from displays of reference quadrilaterals. Pop-out is probably not the proper criterion for defining what a “category” is, but this is the extent to which we can provide an answer to the reviewer’s question.

It would be instructive to investigate stimuli that are on a continuum from representational to geometric, e.g., table tops or cartons under various projections, or balls or buildings that are rectangular or triangular. Building parts, inside and out. like corners. Objects differ from geometric forms in many ways: 3D rather than 2D, more complicated shapes, and internal texture. The geometric figures used are flat, 2-D, but much geometry is 3-D (e. g. cubes) with similar abstract features.

We agree that there is a whole line of potential research here. We decided to start by focusing on the simplest set of geometric shapes that would give us enough variation in geometric regularity while being easy to match on other visual features. We agree with the reviewer that our results should hold both for more complex 2-D shapes, but also for 3-D shapes. Indeed, generative theories of shapes in higher dimensions following similar principles as ours have been devised (I. Biederman, 1987; Leyton, 2003).  We now mention this in the discussion:

“Finally, this research should ultimately be extended to the representation of 3-dimensional geometric shapes, for which similar symbolic generative models have indeed been proposed (Irving Biederman, 1987; Leyton, 2003).”

The feature space of geometry is more than parallelism and symmetry; angles are important, for example. Listing and testing features would be fascinating. Similarly, looking at younger or preferably non-Western children, as Western children are exposed to shapes in play at early ages.

We agree with the reviewer on all point. While we do not list and test the different properties separately in this work, we would like to highlight that angles are part of our geometric feature model, which includes features of “right-angle” and “equal-angles” as suggested by the reviewer.

We also agree about the importance of testing populations with limited exposure to formal training with geometric shapes. This was in fact a core aspect of a previous article of ours which tests both preschoolers, and adults with no access to formal western education – though no non-Western children (Sablé-Meyer et al., 2021). It remains a challenge to perform brain-imaging studies in non-Western populations (although see Dehaene et al., 2010; Pegado et al., 2014).

What in human experience but not the experience of close primates would drive the abstraction of these geometric properties? It's easy to make a case for elaborate brain processes for recognizing and distinguishing things in the world, shared by many species, but the case for brain areas sensitive to processing geometric figures is harder. The fact that these areas are active in blind mathematicians and that they are parietal areas suggests that what is important is spatial far more than visual. Could these geometric figures and their abstract properties be connected in some way to behavior, perhaps with fabrication and construction as well as use? Or with other interactions with complex objects and environments where symmetry and parallelism (and angles and curvature--and weight and size) would be important? Manual dexterity and fabrication also distinguish humans from great apes (quantitatively, not qualitatively), and action drives both visual and spatial representations of objects and spaces in the brain. I certainly wouldn't expect the authors to add research to this already packed paper, but raising some of the conceptual issues would contribute to the significance of the paper.

We refrained from speculating about this point in the previous version of the article, but share some of the reviewers’ intuitions about the underlying drive for geometric abstraction. As described in (Dehaene, 2026; Sablé-Meyer et al., 2022), our hypothesis, which isn’t tested in the present article, is that the emergence of a pervasive ability to represent aspects of the world as compact expressions in a mental “language-of-thought” is what underlies many domains of specific human competence, including some listed by the reviewer (tool construction, scene understanding) and our domain of study here, geometric shapes.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

Overall, I enjoyed reading this paper. It is clearly written and nicely showcases the amount of work that has gone into conducting all these experiments and analyzing the data in sophisticated ways. I also thought the figures were great, and I liked the level of organization in the GitHub repository and am looking forward to seeing the shared data on OpenNeuro. I have some specific questions I hope the authors can address.

(1) Behavior

- Looking at Figure 1, it seemed like most shapes are clustering together, whereas square, rectangle, and maybe rhombus and parallelogram are slightly more unique. I was wondering whether the authors could comment on the potential influence of linguistic labels. Is it possible that it is easier to discard the intruder when the shapes are readily nameable versus not?

This is an interesting observation, but the existence of names for shapes does not suffice to explain all of our findings ; see our reply to the public comment.

(2) fMRI

- As mentioned in the public review, I was surprised that the authors went with an intruder task because I would imagine that performance depends on the specific combination of geometric shapes used within a trial. I assume it is much harder to find, for example, a "Right Hinge" embedded within "Hinge" stimuli than a "Right Hinge" amongst "Squares". In addition, the rotation and scaling of each individual item should affect regular shapes less than irregular shapes, creating visual dissimilarities that would presumably make the task harder. Can the authors comment on how we can be sure that the differences we pick up in the parietal areas are not related to task difficulty but are truly related to geometric shape regularities?

Again, please see our public review response for a larger discussion of the impact of task difficulty. There are two aspects to answering this question.

First, the task is not as the reviewer describes: the intruder task is to find a deviant shape within several slightly rotated and scaled versions of the regular shape it came from. During brain imaging, we did not ask participants to find an exemplar of one of our reference shape amidst copies of another, but rather a deviant version of one shape against copies of its reference version. We only used this intruder task with all pairs of shapes to generate the behavioral RSA matrix.

Second, we agree that some of the fMRI effect may stem from task difficulty, and this motivated our use of RSA analysis in fMRI, and a passive MEG task. RSA results cannot be explained by task difficulty.

Overall, we have tried to make the limitations of the fMRI design, and the motivation for turning to passive presentation in MEG, clearer by stating the issues more clearly when we introduce experiment 4:

“The temporal resolution of fMRI does not allow to track the dynamic of mental representations over time. Furthermore, the previous fMRI experiment suffered from several limitations. First, we studied six quadrilaterals only, compared to 11 in our previous behavioral work. Second, we used an explicit intruder detection, which implies that the geometric regularity effect was correlated with task difficulty, and we cannot exclude that this factor alone explains some of the activations in figure 3C (although it is much less clear how task difficulty alone would explain the RSA results in figure 3D). Third, the long display duration, which was necessary for good task performance especially in children, afforded the possibility of eye movements, which were not monitored inside the 3T scanner and again could have affected the activations in figure 3C.”

- How far in the periphery were the stimuli presented? Was eye-tracking data collected for the intruder task? Similar to the point above, I would imagine that a harder trial would result in more eye movements to find the intruder, which could drive some of the differences observed here.

A 1-degree bar was added to Figure 3A, which faithfully illustrates how the stimuli were presented in fMRI. Eye-tracking data was not collected during fMRI. Although the participants were explicitly instructed to fixate at the center of the screen and avoid eye movements, we fully agree with the referee that we cannot exclude that eye movements were present, perhaps more so for more difficult displays, and would therefore have contributed to the observed fMRI activations in experiment 3 (figure 3C). We now mention this limitation explicity at the end of experiment 3. However, crucially, this potential problem cannot apply to the MEG data. During the MEG task, the stimuli were presented one by one at the center of screen, without any explicit task, thus avoiding issues of eye movements. We therefore consider the MEG geometrical regularity effect, which comes at a relatively early latency (starting at ~160 ms) and even in a passive task, to provide the strongest evidence of geometric coding, unaffected by potential eye movement artefacts. 

- I was wondering whether the authors would consider showing some un-thresholded maps just to see how widespread the activation of the geometric shapes is across all of the cortex.

We share the uncorrected threshold maps in Fig. S3. for both adults and children in the category localizer, copied here as well. For the geometry task, most of the clusters identified are fairly big and survive cluster-corrected permutations; the uncorrected statistical maps look almost fully identical to the one presented in Fig. 3 (p<.001 map).

- I'm missing some discussion on the role of early visual areas that goes beyond the RSA-CNN comparison. I would imagine that early visual areas are not only engaged due to top-down feedback (line 258) but may actually also encode some of the geometric features, such as parallel lines and symmetry. Is it feasible to look at early visual areas and examine what the similarity structure between different shapes looks like?

If early visual areas encoded the geometric features that we propose, then even early sensor-level RSA matrices should show a strong impact of geometric features similarity, which is not what we find (figure 4D). We do, however, appreciate the referee’s request to examine more closely how this similarity structure looks like. We now provide a movie showing the significant correlation between neural activity and our two models (uncorrected participants); indeed, while the early occipital activity (around 110ms) is dominated by a significant correlation with the CNN model, there are also scattered significant sources associated to the symbolic model around these timepoints already.

To test this further, we used beamformers to reconstruct the source-localized activity in calcarine cortex and performed an RSA analysis across that ROI. We find that indeed the CNN model is strongly significant at t=110ms (t=3.43, df=18, p=.003) while the geometric feature model is not (t=1.04, df=18, p=.31), and the CNN is significantly above the geometric feature model (t=4.25, df=18, p<.001). However, this result is not very stable across time, and there are significant temporal clusters around these timepoints associated to each model, with no significant cluster associated to a CNN > geometric (CNN: significant cluster from 88ms to 140ms, p<.001 in permutation based with 10000 permutations; geometric features has a significant cluster from 80ms to 104ms, p=.0475; no significant cluster on the difference between the two).

(3) MEG

- Similar to the fMRI set, I am a little worried that task difficulty has an effect on the decoding results, as the oddball should pop out more in more geometric shapes, making it easier to detect and easier to decode. Can the authors comment on whether it would matter for the conclusions whether they are decoding varying task difficulty or differences in geometric regularity, or whether they think this can be considered similarly?

See above for an extensive discussion of the task difficulty effect. We point out that there is no task in the MEG data collection part. We have clarified the task design by updating our Fig. 4. Additionally, the fact that oddballs are more perceived more or less easily as a function of their geometric regularity is, in part, exactly the point that we are making – but, in MEG, even in the absence of a task of looking for them.

- The authors discuss that the inflated baseline/onset decoding/regression estimates may occur because the shapes are being repeated within a mini-block, which I think is unlikely given the long ISIs and the fact that the geometric features model is not >0 at onset. I think their second possible explanation, that this may have to do with smoothing, is very possible. In the text, it said that for the non-smoothed result, the CNN encoding correlates with the data from 60ms, which makes a lot more sense. I would like to encourage the authors to provide readers with the unsmoothed beta values instead of the 100-ms smoothed version in the main plot to preserve the reason they chose to use MEG - for high temporal resolution!

We fully agree with the reviewer and have accordingly updated the figures to show the unsmoothed data (see below). Indeed, there is now no significant CNN effect before ~60 ms (up to the accuracy of identifying onsets with our method).

- In Figure 4C, I think it would be useful to either provide error bars or show variability across participants by plotting each participant's beta values. I think it would also be nice to plot the dissimilarity matrices based on the MEG data at select timepoints, just to see what the similarity structure is like.

Following the reviewer’s recommendation, we plot the timeseries with SEM as shaded area, and thicker lines for statistically significant clusters, and we provide the unsmoothed version in figure Fig. 4. As for the dissimilarity matrices at select timepoints, this has now been added to figure Fig. 4.

- To evaluate the source model reconstruction, I think the reader would need a little more detail on how it was done in the main text. How were the lead fields calculated? Which data was used to estimate the sources? How are the models correlated with the source data?

We have imported some of the details in the main text as follows (as well as expanding the methods section a little):

“To understand which brain areas generated these distinct patterns of activations, and probe whether they fit with our previous fMRI results, we performed a source reconstruction of our data. We projected the sensor activity onto each participant's cortical surfaces estimated from T1-images. The projection was performed using eLORETA and emptyroom recordings acquired on the same day to estimate noise covariance, with the default parameters of mne-bids-pipeline. Sources were spaced using a recursively subdivided octahedron (oct5). Group statistics were performed after alignement to fsaverage. We then replicated the RSA analysis […]”

- In addition to fitting the CNN, which is used here to model differences in early visual cortex, have the authors considered looking at their fMRI results and localizing early visual regions, extracting a similarity matrix, and correlating that with the MEG and/or comparing it with the CNN model?

We had ultimately decided against comparing the empirical similarity matrices from the MEG and fMRI experiments, first because the stimuli and tasks are different, and second because this would not be directly relevant to our goal, which is to evaluate whether a geometric-feature model accounts for the data. Thus, we systematically model empirical similarity matrices from fMRI and from MEG with our two models derived from different theories of shape perception in order to test predictions about their spatial and temporal dynamic. As for comparing the similarity matrix from early visual regions in fMRI with that predicted by the CNN model, this is effectively visible from our Fig. 3D where we perform searchlight RSA analysis and modeling with both the CNN and the geometric feature model; bilaterally, we find a correlation with the CNN model, although it sometimes overlap with predictions from the geometric feature model as well. We now include a section explaining this reasoning in appendix:

“Representational similarity analysis also offers a way to directly compared similarity matrices measured in MEG and fMRI, thus allowing for fusion of those two modalities and tentatively assigning a “time stamp” to distinct MRI clusters. However, we did not attempt such an analysis here for several reasons. First, distinct tasks and block structures were used in MEG and fMRI. Second, a smaller list of shapes was used in fMRI, as imposed by the slower modality of acquisition. Third, our study was designed as an attempt to sort out between two models of geometric shape recognition. We therefore focused all analyses on this goal, which could not have been achieved by direct MEG-fMRI fusion, but required correlation with independently obtained model predictions.”

Minor comments

- It's a little unclear from the abstract that there is children's data for fMRI only.

We have reworded the abstract to make this unambiguous

- Figures 4a & b are missing y-labels.

We can see how our labels could be confused with (sub-)plot titles and have moved them to make the interpretation clearer.

- MEG: are the stimuli always shown in the same orientation and size?

They are not, each shape has a random orientation and scaling. On top of a task example at the top of Fig. 4, we have now included a clearer mention of this in the main text when we introduce the task:

“shapes were presented serially, one at a time, with small random changes in rotation and scaling parameters, in miniblocks with a fixed quadrilateral shape and with rare intruders with the bottom right corner shifted by a fixed amount (Sablé-Meyer et al., 2021)”

- To me, the discussion section felt a little lengthy, and I wonder whether it would benefit from being a little more streamlined, focused, and targeted. I found that the structure was a little difficult to follow as it went from describing the result by modality (behavior, fMRI, MEG) back to discussing mostly aspects of the fMRI findings.

We have tried to re-organize and streamline the discussion following these comments.

Then, later on, I found that especially the section on "neurophysiological implementation of geometry" went beyond the focus of the data presented in the paper and was comparatively long and speculative.

We have reexamined the discussion, but the citation of papers emphasizing a representation of non-accidental geometric properties in non-human animals was requested by other commentators on our article; and indeed, we think that they are relevant in the context of our prior suggestion that the composition of geometric features might be a uniquely human feature – these papers suggest that individual features may not, and that it is therefore compositionality which might be special to the human brain. We have nevertheless shortened it.

Furthermore, we think that this section is important because symbolic models are often criticized for lack of a plausible neurophysiological implementation. It is therefore important to discuss whether and how the postulated symbolic geometric code could be realized in neural circuits. We have added this justification to the introduction of this section.

Reviewer #2 (Recommendations for the authors):

(1) If the authors want to specifically claim that their findings align with mathematical reasoning, they could at least show the overlap between the activation maps of the current study and those from prior work.

This was added to the fMRI results. See our answers to the public review.

(2) I wonder if the reason the authors only found aIPS in their first analysis (Figure 2) is because they are contrasting geometric shapes with figures that also have geometric properties. In other words, faces, objects, and houses also contain geometric shape information, and so the authors may have essentially contrasted out other areas that are sensitive to these features. One indication that this may be the case is that the geometric regularity effect and searchlight RSA (Figure 3) contains both anterior and posterior IPS regions (but crucially, little ventral activity). It might be interesting to discuss the implications of these differences.

Indeed, we cannot exclude that the few symmetries, perpendicularity and parallelism cues that can be presented in faces, objects or houses were processed as such, perhaps within the ventral pathway, and that these representations would have been subtracted out. We emphasize that our subtraction isolates the geometrical features that are present in simple regular geometric shapes, over and above those that might exist in other categories. We have added this point to the discussion:

“[… ] For instance, faces possess a plane of quasi-symmetry, and so do many other man-made tools and houses. Thus, our subtraction isolated the geometrical features that are present in simple regular geometric shapes (e.g. parallels, right angles, equality of length) over and above those that might already exist, in a less pure form, in other categories.”

(3) I had a few questions regarding the MEG results.

a. I didn't quite understand the task. What is a regular or oddball shape in this context? It's not clear what is being decoded. Perhaps a small example of the MEG task in Figure 4 would help?

We now include an additional sub-figure in Fig. 4 to explain the paradigm. In brief: there is no explicit task, participants are simply asked to fixate. The shapes come in miniblocks of 30 identical reference shapes (up to rotation and scaling), among which some occasional deviant shapes randomly appear (created by moving the corner of the reference shape by some amount).

b. In Figure 4A/B they describe the correlation with a 'symbolic model'. Is this the same as the geometric model in 4C?

It is. We have removed this ambiguity by calling it “geometric model” and setting its color to the one associated to this model thought the article.

c. The author's explanation for why geometric feature coding was slower than CNN encoding doesn't quite make sense to me. As an explanation, they suggest that previous studies computed "elementary features of location or motor affordance", whereas their study work examines "high-level mathematical information of an abstract nature." However, looking at the studies the authors cite in this section, it seems that these studies also examined the time course of shape processing in the dorsal pathway, not "elementary features of location or motor affordance." Second, it's not clear how the geometric feature model reflects high-level mathematical information (see point above about claiming this is related to math).

We thank the referee for pointing out this inappropriate phrase, which we removed. We rephrased the rest of the paragraph to clarify our hypothesis in the following way:

“However, in this work, we specifically probed the processing of geometric shapes that, if our hypothesis is correct, are represented as mental expressions that combine geometrical and arithmetic features of an abstract categorical nature, for instance representing “four equal sides” or “four right angles”. It seems logical that such expressions, combining number, angle and length information, take more time to be computed than the first wave of feedforward processing within the occipito-temporal visual pathway, and therefore only activate thereafter.”

One explanation may be that the authors' geometric shapes require finer-grained discrimination than the object categories used in prior studies. i.e., the odd-ball task may be more of a fine-grained visual discrimination task. Indeed, it may not be a surprise that one can decode the difference between, say, a hammer and a butterfly faster than two kinds of quadrilaterals.

We do not disagree with this intuition, although note that we do not have data on this point (we are reporting and modelling the MEG RSA matrix across geometric shapes only – in this part, no other shapes such as tools or faces are involved). Still, the difference between squares, rectangles, parallelograms and other geometric shapes in our stimuli is not so subtle. Furthermore, CNNs do make very fine grained distinctions, for instance between many different breeds of dogs in the IMAGENET corpus. Still, those sorts of distinctions capture the initial part of the MEG response, while the geometric model is needed only for the later part. Thus, we think that it is a genuine finding that geometric computations associated with the dorsal parietal pathway are slower than the image analysis performed by the ventral occipito-temporal pathway.

d. CNN encoding at time 0 is a little weird, but the author's explanation, that this is explained by the fact that temporal smoothed using a 100 ms window makes sense. However, smoothing by 100 ms is quite a lot, and it doesn't seem accurate to present continuous time course data when the decoding or RSA result at each time point reflects a 100 ms bin. It may be more accurate to simply show unsmoothed data. I'm less convinced by the explanation about shape prediction.

We agree. Following the reviewer’s advice, as well as the recommendation from reviewer 1, we now display unsmoothed plots, and the effects now exhibit a more reasonable timing (Figure 4D), with effects starting around ~60 ms for CNN encoding.

(4) I appreciate the author's use of multiple models and their explanation for why DINOv2 explains more variance than the geometric and CNN models (that it represents both types of features. A variance partitioning analysis may help strengthen this conclusion (Bonner & Epstein, 2018; Lescroart et al., 2015).

However, one difference between DINOv2 and the CNN used here is that it is trained on a dataset of 142 million images vs. the 1.5 million images used in ImageNet. Thus, DINOv2 is more likely to have been exposed to simple geometric shapes during training, whereas standard ImageNet trained models are not. Indeed, prior work has shown that lesioning line drawing-like images from such datasets drastically impairs the performance of large models (Mayilvahanan et al., 2024). Thus, it is unlikely that the use of a transformer architecture explains the performance of DINOv2. The authors could include an ImageNet-trained transformer (e.g., ViT) and a CNN trained on large datasets (e.g., ResNet trained on the Open Clip dataset) to test these possibilities. However, I think it's also sufficient to discuss visual experience as a possible explanation for the CNN and DINOv2 results. Indeed, young children are exposed to geometric shapes, whereas ImageNet-trained CNNs are not.

We agree with the reviewer’s observation. In fact, new and ongoing work from the lab is also exploring this; we have included in supplementary materials exactly what the reviewer is suggesting, namely the time course of the correlation with ViT and with ConvNeXT. In line with the reviewers’ prediction, these networks, trained on much larger dataset and with many more parameters, can also fit the human data as well as DINOv2. We ran additional analysis of the MEG data with ViT and ConvNeXT, which we now report in Fig. S6 as well as in an additional sentence in that section:

“[…] similar results were obtained by performing the same analysis, not only with another vision transformer network, ViT, but crucially using a much larger convolutional neural network, ConvNeXT, which comprises ~800M parameters and has been trained on 2B images, likely including many geometric shapes and human drawings. For the sake of completeness, RSA analysis in sensor space of the MEG data with these two models is provided in Fig. S6.”

We conclude that the size and nature of the training set could be as important as the architecture – but also note that humans do not rely on such a huge training set. We have updated the text, as well as Fig. S6, accordingly by updating the section now entitled “Vision Transformers and Larger Neural Networks”, and the discussion section on theoretical models.

(5) The authors may be interested in a recent paper from Arcaro and colleagues that showed that the parietal cortex is greatly expanded in humans (including infants) compared to non-human primates (Meyer et al., 2025), which may explain the stronger geometric reasoning abilities of humans.

A very interesting article indeed! We have updated our article to incorporate this reference in the discussion, in the section on visual pathways, as follows:

“Finally, recent work shows that within the visual cortex, the strongest relative difference in growth between human and non-human primates is localized in parietal areas (Meyer et al., 2025). If this expansion reflected the acquisition of new processing abilities in these regions, it  might explain the observed differences in geometric abilities between human and non-human primates (Sablé-Meyer et al., 2021).”

Also, the authors may want to include this paper, which uses a similar oddity task and compelling shows that crows are sensitive to geometric regularity:

Schmidbauer, P., Hahn, M., & Nieder, A. (2025). Crows recognize geometric regularity. Science Advances, 11(15), eadt3718. https://doi.org/10.1126/sciadv.adt3718

We have ongoing discussions with the authors of this work and are  have prepared a response to their findings (Sablé-Meyer and Dehaene, 2025)–ultimately, we think that this discussion, which we agree is important, does not have its place in the present article. They used a reduced version of our design, with amplified differences in the intruders. While they did not test the fit of their model with CNN or geometric feature models, we did and found that a simple CNN suffices to account for crow behavior. Thus, we disagree that their conclusions follow from their results and their conclusions. But the present article does not seem to be the right platform to engage in this discussion.

References

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Dehaene, S., & Brannon, E. (2011). Space, time and number in the brain: Searching for the foundations of mathematical thought. Academic Press.

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Freud, E., Plaut, D. C., & Behrmann, M. (2016). 'What 'is happening in the dorsal visual pathway. Trends in Cognitive Sciences, 20(10), 773-784.

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Han, Z., & Sereno, A. (2022). Modeling the Ventral and Dorsal Cortical Visual Pathways Using Artificial Neural Networks. Neural Computation, 34(1), 138-171. https://doi.org/10.1162/neco_a_01456

Janssen, P., Srivastava, S., Ombelet, S., & Orban, G. A. (2008). Coding of shape and position in macaque lateral intraparietal area. Journal of Neuroscience, 28(26), 6679-6690.

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Lescroart, M. D., Stansbury, D. E., & Gallant, J. L. (2015). Fourier power, subjective distance, and object categories all provide plausible models of BOLD responses in scene-selective visual areas. Frontiers in Computational Neuroscience, 9(135), 1-20. https://doi.org/10.3389/fncom.2015.00135

Mayilvahanan, P., Zimmermann, R. S., Wiedemer, T., Rusak, E., Juhos, A., Bethge, M., & Brendel, W. (2024). In search of forgotten domain generalization. arXiv Preprint arXiv:2410.08258.

Meyer, E. E., Martynek, M., Kastner, S., Livingstone, M. S., & Arcaro, M. J. (2025). Expansion of a conserved architecture drives the evolution of the primate visual cortex. Proceedings of the National Academy of Sciences, 122(3), e2421585122. https://doi.org/10.1073/pnas.2421585122

Orban, G. A. (2011). The extraction of 3D shape in the visual system of human and nonhuman primates. Annual Review of Neuroscience, 34, 361-388.

Romei, V., Driver, J., Schyns, P. G., & Thut, G. (2011). Rhythmic TMS over Parietal Cortex Links Distinct Brain Frequencies to Global versus Local Visual Processing. Current Biology, 21(4), 334-337. https://doi.org/10.1016/j.cub.2011.01.035

Sereno, A. B., & Maunsell, J. H. R. (1998). Shape selectivity in primate lateral intraparietal cortex. Nature, 395(6701), 500-503. https://doi.org/10.1038/26752

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Van Dromme, I. C., Premereur, E., Verhoef, B.-E., Vanduffel, W., & Janssen, P. (2016). Posterior Parietal Cortex Drives Inferotemporal Activations During Three-Dimensional Object Vision. PLoS Biology, 14(4), e1002445. https://doi.org/10.1371/journal.pbio.1002445

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Reviewer #3 (Recommendations for the authors):

Bring into the discussion some of the issues outlined above, especially a) the spatial rather than visual of the geometric figures and b) the non-representational aspects of geometric form aspects.

We thank the reviewer for their recommendations – see our response to the public review for more details.

Author response:

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

Reviewer #1 (Public review):

Summary:

This paper presents two experiments, both of which use a target detection paradigm to investigate the speed of statistical learning. The first experiment is a replication of Batterink, 2017, in which participants are presented with streams of uniform-length, trisyllabic nonsense words and asked to detect a target syllable. The results replicate previous findings, showing that learning (in the form of response time facilitation to later-occurring syllables within a nonsense word) occurs after a single exposure to a word. In the second experiment, participants are presented with streams of variable-length nonsense words (two trisyllabic words and two disyllabic words) and perform the same task. A similar facilitation effect was observed as in Experiment 1. The authors interpret these findings as evidence that target detection requires mechanisms different from segmentation. They present results of a computational model to simulate results from the target detection task and find that an "anticipation mechanism" can produce facilitation effects, without performing segmentation. The authors conclude that the mechanisms involved in the target detection task are different from those involved in the word segmentation task.

Strengths:

The paper presents multiple experiments that provide internal replication of a key experimental finding, in which response times are facilitated after a single exposure to an embedded pseudoword. Both experimental data and results from a computational model are presented, providing converging approaches for understanding and interpreting the main results. The data are analyzed very thoroughly using mixed effects models with multiple explanatory factors.

Weaknesses:

In my view, the main weaknesses of this study relate to the theoretical interpretation of the results.

(1) The key conclusion from these findings is that the facilitation effect observed in the target detection paradigm is driven by a different mechanism (or mechanisms) than those involved in word segmentation. The argument here I think is somewhat unclear and weak, for several reasons:

First, there appears to be some blurring in what exactly is meant by the term "segmentation" with some confusion between segmentation as a concept and segmentation as a paradigm.

Conceptually, segmentation refers to the segmenting of continuous speech into words. However, this conceptual understanding of segmentation (as a theoretical mechanism) is not necessarily what is directly measured by "traditional" studies of statistical learning, which typically (at least in adults) involve exposure to a continuous speech stream followed by a forced-choice recognition task of words versus recombined foil items (part-words or nonwords). To take the example provided by the authors, a participant presented with the sequence GHIABCDEFABCGHI may endorse ABC as being more familiar than BCG, because ABC is presented more frequently together and the learned association between A and B is stronger than between C and G. However, endorsement of ABC over BCG does not necessarily mean that the participant has "segmented" ABC from the speech stream, just as faster reaction times in responding to syllable C versus A do not necessarily indicate successful segmentation. As the authors argue on page 7, "an encounter to a sequence in which two elements co-occur (say, AB) would theoretically allow the learner to use the predictive relationship during a subsequent encounter (that A predicts B)." By the same logic, encoding the relationship between A and B could also allow for the above-chance endorsement of items that contain AB over items containing a weaker relationship.

Both recognition performance and facilitation through target detection reflect different outcomes of statistical learning. While they may reflect different aspects of the learning process and/or dissociable forms of memory, they may best be viewed as measures of statistical learning, rather than mechanisms in and of themselves.

Thanks for this nuanced discussion, and this is an important point that R2 also raised. We agree that segmentation can refer to both an experimental paradigm and a mechanism that accounts for learning in the experimental paradigm. In the experimental paradigm, participants are asked to identify which words they believe to be (whole) words from the continuous syllable stream. In the target-detection experimental paradigm, participants are not asked to identify words from continuous streams, and instead, they respond to the occurrences of a certain syllable. It’s possible that learners employ one mechanism in these two tasks, or that they employ separate mechanisms. It’s also the case that, if all we have is positive evidence for both experimental paradigms, i.e., learners can succeed in segmentation tasks as well as in target detection tasks with different types of sequences, we would have no way of talking about different mechanisms, as you correctly suggested that evidence for segmenting AB and processing B faster following A, is not evidence for different mechanisms.

However, that is not the case. When the syllable sequences contain same-length subsequences (i.e., words), learning is indeed successful in both segmentation and target detection tasks. However, in studies such as Hoch et al. (2013), findings suggest that words from mixed-length sequences are harder to segment than words from uniform-length sequences. This finding exists in adult work (e.g., Hoch et al. 2013) as well as infant work (Johnson & Tyler, 2010), and replicated here in the newly included Experiment 3, which stands in contrast to the positive findings of the facilitation effect with mixed-length sequences in the target detection paradigm (one of our main findings in the paper). Thus, it seems to be difficult to explain, if the learning mechanisms were to be the same, why humans can succeed in mixed-length sequences in target detection (as shown in Experiment 2) but fail in uniform-length sequences (as shown in Hoch et al. and Experiment 3).

In our paper, we have clarified these points describe the separate mechanisms in more detail, in both the Introduction and General Discussion sections.

(2) The key manipulation between experiments 1 and 2 is the length of the words in the syllable sequences, with words either constant in length (experiment 1) or mixed in length (experiment 2). The authors show that similar facilitation levels are observed across this manipulation in the current experiments. By contrast, they argue that previous findings have found that performance is impaired for mixed-length conditions compared to fixed-length conditions. Thus, a central aspect of the theoretical interpretation of the results rests on prior evidence suggesting that statistical learning is impaired in mixed-length conditions. However, it is not clear how strong this prior evidence is. There is only one published paper cited by the authors - the paper by Hoch and colleagues - that supports this conclusion in adults (other mentioned studies are all in infants, which use very different measures of learning). Other papers not cited by the authors do suggest that statistical learning can occur to stimuli of mixed lengths (Thiessen et al., 2005, using infant-directed speech; Frank et al., 2010 in adults). I think this theoretical argument would be much stronger if the dissociation between recognition and facilitation through RTs as a function of word length variability was demonstrated within the same experiment and ideally within the same group of participants.

To summarize the evidence of learning uniform-length and mixed-length sequences (which we discussed in the Introduction section), “even though infants and adults alike have shown success segmenting syllable sequences consisting of words that were uniform in length (i.e., all words were either disyllabic; Graf Estes et al., 2007; or trisyllabic, Aslin et al., 1998), both infants and adults have shown difficulty with syllable sequences consisting of words of mixed length (Johnson & Tyler, 2010; Johnson & Jusczyk, 2003a; 2003b; Hoch et al., 2013).” The newly added Experiment 3 also provided evidence for the difference in uniform-length and mixed-length sequences. Notably, we do not agree with the idea that infant work should be disregarded as evidence just because infants were tested with habituation methods; not only were the original findings (Saffran et al. 1996) based on infant work, so were many other studies on statistical learning.

There are other segmentation studies in the literature that have used mixed-length sequences, which are worth discussing. In short, these studies differ from the Saffran et al. (1996) studies in many important ways, and in our view, these differences explain why the learning was successful. Of interest, Thiessen et al. (2005) that you mentioned was based on infant work with infant methods, and demonstrated the very point we argued for: In their study, infants failed to learn when mixed-length sequences were pronounced as adult-directed speech, and succeeded in learning given infant-directed speech, which contained prosodic cues that were much more pronounced. The fact that infants failed to segment mixed-length sequences without certain prosodic cues is consistent with our claim that mixed-length sequences are difficult to segment in a segmentation paradigm. Another such study is Frank et al. (2010), where continuous sequences were presented in “sentences”. Different numbers of words were concatenated into sentences where a 500ms break was present between each sentence in the training sequence. One sentence contained only one word, or two words, and in the longest sentence, there were 24 words. The results showed that participants are sensitive to the effect of sentence boundaries, which coincide with word boundaries. In the extreme, the one-word-per-sentence condition simply presents learners with segmented word forms. In the 24-word-per-sentence condition, there are nevertheless sentence boundaries that are word boundaries, and knowing these word boundaries alone should allow learners to perform above chance in the test phase. Thus, in our view, this demonstrates that learners can use sentence boundaries to infer word boundaries, which is an interesting finding in its own right, but this does not show that a continuous syllable sequence with mixed word lengths is learnable without additional information. In summary, to our knowledge, syllable sequences containing mixed word lengths are better learned when additional cues to word boundaries are present, and there is strong evidence that syllable sequences containing uniform-word lengths are learned better than mixed-length ones.

Frank, M. C., Goldwater, S., Griffiths, T. L., & Tenenbaum, J. B. (2010). Modeling human performance in statistical word segmentation. Cognition, 117(2), 107-125.

To address your proposal of running more experiments to provide stronger evidence for our theory, we were planning to run another study to have the same group of participants do both the segmentation and target detection paradigm as suggested, but we were unable to do so as we encountered difficulties to run English-speaking participants. Instead, we have included an experiment (now Experiment 3), showing the difference between the learning of uniform-length and mixed-length sequences with the segmentation paradigm that we have never published previously. This experiment provides further evidence for adults’ difficulties in segmenting mixed-length sequences.

(3) The authors argue for an "anticipation" mechanism in explaining the facilitation effect observed in the experiments. The term anticipation would generally be understood to imply some kind of active prediction process, related to generating the representation of an upcoming stimulus prior to its occurrence. However, the computational model proposed by the authors (page 24) does not encode anything related to anticipation per se. While it demonstrates facilitation based on prior occurrences of a stimulus, that facilitation does not necessarily depend on active anticipation of the stimulus. It is not clear that it is necessary to invoke the concept of anticipation to explain the results, or indeed that there is any evidence in the current study for anticipation, as opposed to just general facilitation due to associative learning.

Thanks for raising this point. Indeed, the anticipation effect we reported is indistinguishable from the facilitation effect that we reported in the reported experiments. We have dropped this framing.

In addition, related to the model, given that only bigrams are stored in the model, could the authors clarify how the model is able to account for the additional facilitation at the 3rd position of a trigram compared to the 2nd position?

Thanks for the question. We believe it is an empirical question whether there is an additional facilitation at the 3rd position of a trigram compared to the 2nd position. To investigate this issue, we conducted the following analysis with data from Experiment 1. First, we combined the data from two conditions (exact/conceptual) from Experiment 1 so as to have better statistical power. Next, we ran a mixed effect regression with data from syllable positions 2 and 3 only (i.e., data from syllable position 1 were not included). The fixed effect included the two-way interaction between syllable position and presentation, as well as stream position, and the random effect was a by-subject random intercept and stream position as the random slope. This interaction was significant (χ²(3) =11.73, p=0.008), suggesting that there is additional facilitation to the 3rd position compared to the 2nd position.

For the model, here is an explanation of why the model assumes an additional facilitation to the 3rd position. In our model, we proposed a simple recursive relation between the RT of a syllable occurring for the nth time and the n+1^th time, which is:

and

RT(1) = RT0 + stream_pos * stream_inc, where the n in RT(n) represents the RT for the n^th presentation of the target syllable, stream_pos is the position (3-46) in the stream, and occurrence is the number of occurrences that the syllable has occurred so far in the stream.

What this means is that the model basically provides an RT value for every syllable in the stream. Thus, for a target at syllable position 1, there is a RT value as an unpredictable target, and for targets at syllable position 2, there is a facilitation effect. For targets at syllable position 3, it is facilitated the same amount. As such, there is an additional facilitation effect for syllable position 3 because effects of predication are recursive.

(4) In the discussion of transitional probabilities (page 31), the authors suggest that "a single exposure does provide information about the transitions within the single exposure, and the probability of B given A can indeed be calculated from a single occurrence of AB." Although this may be technically true in that a calculation for a single exposure is possible from this formula, it is not consistent with the conceptual framework for calculating transitional probabilities, as first introduced by Saffran and colleagues. For example, Saffran et al. (1996, Science) describe that "over a corpus of speech there are measurable statistical regularities that distinguish recurring sound sequences that comprise words from the more accidental sound sequences that occur across word boundaries. Within a language, the transitional probability from one sound to the next will generally be highest when the two sounds follow one another within a word, whereas transitional probabilities spanning a word boundary will be relatively low." This makes it clear that the computation of transitional probabilities (i.e., Y | X) is conceptualized to reflect the frequency of XY / frequency of X, over a given language inventory, not just a single pair. Phrased another way, a single exposure to pair AB would not provide a reliable estimate of the raw frequencies with which A and AB occur across a given sample of language.

Thanks for the discussion. We understand your argument, but we respectively disagree that computing transitional probabilities must be conducted under a certain theoretical framework. In our humble opinion, computing transitional probabilities is a mathematical operation, and as such, it is possible to do so with the least amount of data possible that enables the mathematical operation, which concretely is a single exposure during learning. While it is true that a single exposure may not provide a reliable estimate of frequencies or probabilities, it does provide information with which the learner can make decisions.

This is particularly true for topics under discussion regarding the minimal amount of exposure that can enable learning. It is important to distinguish the following two questions: whether learners can learn from a short exposure period (from a single exposure, in fact) and how long of an exposure period does the learner require for it to be considered to produce a reliable estimate of frequencies. Incidentally, given the fact that learners can learn from a single exposure based on Batterink (2017) and the current study, it does not appear that learners require a long exposure period to learn about transitional probabilities.

(5) In experiment 2, the authors argue that there is robust facilitation for trisyllabic and disyllabic words alike. I am not sure about the strength of the evidence for this claim, as it appears that there are some conflicting results relevant to this conclusion. Notably, in the regression model for disyllabic words, the omnibus interaction between word presentation and syllable position did not reach significance (p= 0.089). At face value, this result indicates that there was no significant facilitation for disyllabic words. The additional pairwise comparisons are thus not justified given the lack of omnibus interaction. The finding that there is no significant interaction between word presentation, word position, and word length is taken to support the idea that there is no difference between the two types of words, but could also be due to a lack of power, especially given the p-value (p = 0.010).

Thanks for the comment. Firstly, we believe there is a typo in your comment, where in the last sentence, we believe you were referring to the p-value of 0.103 (source: “The interaction was not significant (χ2(3) = 6.19, p= 0.103”). Yes, a null result with a frequentist approach cannot support a null claim, but Bayesian analyses could potentially provide evidence for the null.

To this end, we conducted a Bayes factor analysis using the approach outlined in Harms and Lakens (2018), which generates a Bayes factor by computing a Bayesian information criterion for a null model and an alternative model. The alternative model contained a three-way interaction of word length, word presentation, and word position, whereas the null model contained a two-way interaction between word presentation and word position as well as a main effect of word length. Thus, the two models only differ in terms of whether there is a three-way interaction. The Bayes factor is then computed as exp[(BICalt − BICnull)/2]. This analysis showed that there is strong evidence for the null, where the Bayes Factor was found to be exp(25.65) which is more than 1011. Thus, there is no power issue here, and there is strong evidence for the null claim that word length did not interact with other factors in Experiment 2.

There is another issue that you mentioned, of whether we should conduct pairwise comparisons if the omnibus interaction did not reach significance. This would be true given the original analysis plan, but we believe that a revised analysis plan makes more sense. In the revised analysis plan for Experiment 2, we start with the three-way interaction (as just described in the last paragraph). The three-way interaction was not significant, and after dropping the third interaction terms, the two-way interaction and the main effect of word length are both significant, and we use this as the overall model. Testing the significance of the omnibus interaction between presentation and syllable position, we found that this was significant (χ²(3) =49.77, p<0.001). This represents that, in one model, that the interaction between presentation and syllable position using data from both disyllabic and trisyllabic words. This was in addition to a significant fixed effect of word length (β=0.018, z=6.19, p<0.001). This should motivate the rest of the planned analysis, which regards pairwise comparisons in different word length conditions.

(6) The results plotted in Figure 2 seem to suggest that RTs to the first syllable of a trisyllabic item slow down with additional word presentations, while RTs to the final position speed up. If anything, in this figure, the magnitude of the effect seems to be greater for 1st syllable positions (e.g., the RT difference between presentation 1 and 4 for syllable position 1 seems to be numerically larger than for syllable position 3, Figure 2D). Thus, it was quite surprising to see in the results (p. 16) that RTs for syllable position 1 were not significantly different for presentation 1 vs. the later presentations (but that they were significant for positions 2 and 3 given the same comparison). Is this possibly a power issue? Would there be a significant slowdown to 1st syllables if results from both the exact replication and conceptual replication conditions were combined in the same analysis?

Thanks for the suggestion and your careful visual inspection of the data. After combining the data, the slowdown to 1st syllables is indeed significant. We have reported this in the results of Experiment 1 (with an acknowledgement to this review):

Results showed that later presentations took significantly longer to respond to compared to the first presentation (χ²(3) = 10.70, p=0.014), where the effect grew larger with each presentation (second presentation: β=0.011, z=1.82, p=0.069; third presentation: β=0.019, z=2.40, p=0.016; fourth presentation: β=0.034, z=3.23, p=0.001).

(7) It is difficult to evaluate the description of the PARSER simulation on page 36. Perhaps this simulation should be introduced earlier in the methods and results rather than in the discussion only.

Thanks for the suggestions. We have added two separate simulations in the paper, which should describe the PARSER simulations sufficiently, as well as provide further information on the correspondence between the simulations and the experiments. Thanks again for the great review! We believe our paper has improved significantly as a result.

Author response:

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

Reviewer #1 (Public review):

This study investigates how ant group demographics influence nest structures and group behaviors of Camponotus fellah ants, a ground-dwelling carpenter ant species (found locally in Israel) that build subterranean nest structures. Using a quasi-2D cell filled with artificial sand, the authors perform two complementary sets of experiments to try to link group behavior and nest structure: first, the authors place a mated queen and several pupae into their cell and observe the structures that emerge both before and after the pupae eclose (i.e., "colony maturation" experiments); second, the authors create small groups (of 5,10, or 15 ants, each including a queen) within a narrow age range (i.e., "fixed demographic" experiments) to explore the dependence of age on construction. Some of the fixed demographic instantiations included a manually induced catastrophic collapse event; the authors then compared emergency repair behavior to natural nest creation. Finally, the authors introduce a modified logistic growth model to describe the time-dependent nest area. The modification introduced parameters that allow for age-dependent behavior, and the authors use their fixed demographic experiments to set these parameters, and then apply the model to interpret the behavior of the colony maturation experiments. The main results of this paper are that for natural nest construction, nest areas, and morphologies depend on the age demographics of ants in the experiments: younger ants create larger nests and angled tunnels, while older ants tend to dig less and build predominantly vertical tunnels; in contrast, emergency response seems to elicit digging in ants of all ages to repair the nest.

The experimental results are solid, providing new information and important insights into nest and colony growth in a social insect species. As presented, I still have some reservations about the model's contribution to a deeper understanding of the system. Additional context and explanation of the model, implications, and limitations would be helpful for readers.

We sincerely thank Reviewer #1 for the time and effort dedicated to our manuscript's detailed review and assessment. The new revision suggestions were constructive, and we have provided a point-by-point response to address them.

Reviewer #2 (Public review):

I enjoyed this paper and its examination of the relationship between overall density and age polyethism to reduce the computational complexity required to match nest size with population. I had some questions about the requirement that growth is infinite in such a solution, but these have been addressed by the authors in the responses and the updated manuscript. I also enjoyed the discussion of whether collective behaviour is an appropriate framework in systems in which agents (or individuals) differ in the behavioural rules they employ, according to age, location, or information state. This is especially important in a system like social insects, typically held as a classic example of individual-as-subservient to whole, and therefore most likely to employ universal rules of behaviour. The current paper demonstrates a potentially continuous age-related change in target behaviour (excavation), and suggests an elegant and minimal solution to the requirement for building according to need in ants, avoiding the invocation of potentially complex cognitive mechanisms, or information states that all individuals must have access to in order to have an adaptive excavation output.

The authors have addressed questions I had in the review process and the manuscript is now clear in its communication and conclusions.

The modelling approach is compelling, also allowing extrapolation to other group sizes and even other species. This to me is the main strength of the paper, as the answer to the question of whether it is younger or older ants that primarily excavate nests could have been answered by an individual tracking approach (albeit there are practical limitations to this, especially in the observation nest setup, as the authors point out). The analysis of the tunnel structure is also an important piece of the puzzle, and I really like the overall study.

We sincerely thank Reviewer #2 for the time and effort dedicated to our manuscript's detailed review and assessment.  

Reviewer #1 (Recommendations for the authors):

Thank you for the modifications. I found much of the additional information very helpful. I do still have a few comments, which I will include below.

We thank the reviewer for this comment

The authors provide some additional citations for the model, however, the ODE in refs 24 and 30 is different from what the authors present here, and different from what is presented in ref 29. Specifically, the additional "volume" term that multiplies the entire equation. Can the authors provide some additional context for their model in comparison to these models as well as how their model relates to other work?

We thank the reviewer for this question. The primary difference between the logistic model (reference number: 24,30), and the saturation model (reference number: 29) is rooted in their assumptions on the scaling of the active number of ants that participate in the nest excavation and the nest volume.

The logistic growth model ( 𝑑𝑉/𝑑𝑡 = α𝑉(1-V/Vs) describes the excavation in fixed-sized colonies (50, 100, 200) through a balance of two key processes : (1) positive feedback (α𝑉), where the digging efficiency increases with the nest size, and (2) negative feedback (1-V/Vs), where growth slows as the nest approaches a saturation (Vs). The model assumes that the number of actively excavating ants is linearly proportional to the nest volume (V). This represents a scenario where a large nest contains or can support more workers, which in turn increases the digging rates. While this does not require explicit communication between individuals, ants indirectly sense the global nest volume through stigmergic cues, such as pheromone depositions, encounter rates, while ignoring individual differences in age. 

In contrast, the saturation model (𝑑𝑉/𝑑𝑡 = α𝑉(1-V/Vs)  assumes a constant number of ants is working throughout the excavation. The digging rate is therefore independent of the nest volume, this model imposes a different cognitive requirement ants must somehow assess the global nest slowing only due to the saturation term (1-V/Vs) as the nest approaches its target size. However, volume (V) and the overall number of ants in the nest. Thus, rather than relying on local cues, ants need more explicit communication or a sophisticated global perception mechanism that allows ants to sense the nest volume and the nest population to adjust the digging rates accordingly. Therefore, this model requires a more complex and less biologically plausible mechanism than the logistic model.

In our age-dependent digging model in the manuscript, we explicitly sum the contribution of each ant towards the nest area expansion based on its age-dependent digging threshold (quantified from fixed demographics experiments) the sum over Thus, the term ‘V’ in the ‘ 𝑉(1-V/Vs) takes the same effect as sum over all ants in the equation (2) of our manuscript; they describe how the total excavation rate scales with the number of individuals. Under the simplifying assumption that the number of ants is proportional to the nest volume ‘V’, and that all ants dig at a constant rate, our equation (2) in the manuscript reduces to the logistic equation ‘𝑉(1-V/Vs)’ This implies that each ant individually assesses the nest volume and then digs at a rate ‘(1-V/Vs)’.

Thus, we adopted the simpler model from the previously published ones, in which ants individually react to the local density cues and regulate their digging. This approach does not require a global assessment of the nest volume or the number of ants; a local perception of density triggers each ant’s decision to dig, likely modulated by the frequency of social contacts or chemical concentration, which serves as an indicator of the global nest area. The ant compares this locally perceived density to an innate, age-specific threshold. If the perceived local density exceeds its threshold (indicating insufficient area), it digs; otherwise, there is no digging. Thus, excavation dynamics in maturing colonies emerge from this collective response to local density cues, without any individual need to directly assess the global nest volume (V) or having explicit knowledge of the colony size (N).

As suggested by the reviewer, we have added these points to the discussion, contrasting the previously published models with our age-dependent excavation models (line numbers: 283-290) “In our study, we adopted the simpler version of previously published age-independent excavation models, where individuals respond to local stigmergic cues such as encounter rates or pheromone concentrations, which serve as a proxy for the global nest volume (24,30). We minimally modified this model to include age-dependent density targets. According to our age-dependent digging model, each ant compares this perceived local density to its own innate age-specific digging threshold as quantified from the fixed demographics experiments. If the perceived local density exceeds its age-dependent area threshold (indicating insufficient area), it digs; otherwise, there is no digging. This mechanism eliminates the need for cognitively demanding global assessment of the total nest volume or the overall colony population, a requirement for the saturation model (29)”. 

I still find it a little concerning that the age-independent model, though it cannot be correct, fits the data better than the age-dependent modification. It seems to me the models presented in refs 24, 29, and 30, which served as inspiration for the one presented here, do not have any deep theoretical origin, but were chosen for "being consistent with" the observed overall excavated volumes. Is this correct, and if so, how much can/should be gleaned about behavior from these models? Please provide some discussion of what is reasonable to expect from such a model as well as what the limitations might be.

We thank the reviewer for the comment. 

In our study, we make an important assumption, as described in the lines (line number : 161 - 164) of the manuscript, that ants rely on local cues during nest excavation, and individuals cannot distinguish between the fixed demographics and colony maturation conditions. This implies that the age-dependent target area identified in the fixed demographics experiments should also account for the excavation dynamics seen in the colony maturation experiments. 

From the fixed demographics young and old experiments, we directly quantified that the younger ants excavate a significantly larger area than the older ants for the same group size. This age-dependent digging propensity is an experimental result, and not a model output. 

We agree that the age-independent model fits the colony maturation experiments well, even though it's not a statistically better fit than the age-dependent model. However, the age-independent models in the references (24,29,30) fail to explain the empirically obtained excavation dynamics in the fixed demographics, young and old colonies. If indeed these models were true, then we would have observed similar excavated areas between the colony maturation, fixed demographics, young, and older colonies of the same size. Thus, the inconsistency of these models confirms that age-independent assumptions are biologically inadequate. These details are explicitly mentioned in lines (304 - 309).

We believe that our model’s value is in providing a plausible explanation for the observed excavation dynamics in the colony maturation experiments, and generating testable predictions (Figure 4. C, and 4.D,  described in lines 199 - 216) about the percentage contribution of different age cohorts and queens to the excavated area from the colony maturation experiments. This prediction would not be possible with an age-independent model.

Minor comments:

Figure 2A: Please use a color other than white for the model... this curve is still very hard to see

We thank the reviewer for the comment. The colour is changed to yellow. 

Figure 4A: Should quoted confidence intervals for slope and intercept be swapped?

Yes, we thank the reviewer for pointing this out. The labels for the slope and intercept were swapped. We corrected this in the current revised version 2. 

Figure 5 D-F: Can the authors show data points and confidence intervals instead of bar graphs? The error bars dipping below zero do not clearly represent the data.

We thank the reviewer for the comment. We now show the individual data points from each treatment with the 95% Confidence Interval of the mean.

Author response:

We sincerely thank the reviewers and editors for their thoughtful evaluations of our work. We are grateful for the careful reading, constructive critiques, and encouraging comments regarding the electrophysiological analyses, mutagenesis, and vascular experiments. The suggestions provided have been very helpful, and we are working to address these points in our revision to strengthen the manuscript and improve its clarity.

In revising the manuscript, we plan to clarify several text passages as recommended by the reviewers, and review and refine the discussion for improved precision. Following the suggestions of the reviewers, we plan to perform a number of additional experiments to provide more data for the binding region and for further mechanistic and physiological insight. We will prepare a point-by-point response addressing all issues raised in a detailed rebuttal. Additionally, we will include improvements in the Methods section as suggested by the SciScore core report.

We appreciate the opportunity to revise our work and thank the reviewers again for their valuable feedback.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors used a coarse-grained DNA model (cgNA+) to explore how DNA sequences and CpG methylation/hydroxymethylation influence nucleosome wrapping energy and the probability density of optimal nucleosomal configuration. Their findings indicate that both methylated and hydroxymethylated cytosines lead to increased nucleosome wrapping energy. Additionally, the study demonstrates that methylation of CpG islands increases the probability of nucleosome formation.

Strengths:

The major strength of this method is the model explicitly includes phosphate group as DNA-histone binding site constraints, enhancing CG model accuracy and computational efficiency and allowing comprehensive calculations of DNA mechanical properties and deformation energies.

Weaknesses:

A significant limitation of this study is that the parameter sets for the methylated and hydroxymethylated CpG steps in the cgNA+ model are derived from all-atom molecular dynamics (MD) simulations that use previously established force field parameters for modified cytosines (P´erez A, et al. Biophys J. 2012; Battistini, et al. PLOS Comput Biol. 2021). These parameters suggest that both methylated and hydroxymethylated cytosines increase DNA stiffness and nucleosome wrapping energy, which could predispose the coarse-grained model to replicate these findings. Notably, conflicting results from other all-atom MD simulations, such as those by Ngo T in Nat. Commun. 2016, shows that hydroxymethylated cytosines increase DNA flexibility, contrary to methylated cytosines. If the cgNA+ model were trained on these later parameters or other all-atom MD force fields, different conclusions might be obtained regarding the effects of methylated and hydroxymethylation on nucleosome formation.

Despite the training parameters of the cgNA+ model, the results presented in the manuscript indicate that methylated cytosines increase both DNA stiffness and nucleosome wrapping energy. However, when comparing nucleosome occupancy scores with predicted nucleosome wrapping energies and optimal configurations, the authors find that methylated CGIs exhibit higher nucleosome occupancies than unmethylated ones, which seems to contradict the expected relationship where increased stiffness should reduce nucleosome formation affinity. In the manuscript, the authors also admit that these conclusions “apparently runs counter to the (perhaps naive) intuition that high nucleosome forming affinity should arise for fragments with low wrapping energy”. Previous all-atom MD simulations (P´erez A, et al. Biophys J. 2012; Battistini, et al. PLOS Comput Biol. 202; Ngo T, et al. Nat. Commun. 20161) show that the stiffer DNA upon CpG methylation reduces the affinity of DNA to assemble into nucleosomes or destabilizes nucleosomes. Given these findings, the authors need to address and reconcile these seemingly contradictory results, as the influence of epigenetic modifications on DNA mechanical properties and nucleosome formation are critical aspects of their study.

Understanding the influence of sequence-dependent and epigenetic modifications of DNA on mechanical properties and nucleosome formation is crucial for comprehending various cellular processes. The authors’ study, focusing on these aspects, definitely will garner interest from the DNA methylation research community.

Training the cgNA+ model on alternative MD simulation datasets is certainly of interest to us. However, due to the significant computational cost, this remains a goal for future work. The relationship between nucleosome occupancy scores and nucleosome wrapping energy is still debated, as noted in our Discussion section. The conflicting results may reflect differences in experimental conditions and the contribution of cellular factors other than DNA mechanics to nucleosome formation in vivo. For instance, P´erez et al. (2012), Battistini et al. (2021), and Ngo et al. (2016) concluded that DNA methylation reduces nucleosome formation based on experiments with modified Widom 601 sequences. In contrast, the genome-wide methylation study by Collings and Anderson (2017) found the opposite effect. In our work, we also use whole-genome nucleosome occupancy data.

Comments on revised version:

The authors have addressed most of my comments and concerns regarding this manuscript.

Reviewer #2 (Public Review):

Summary:

This study uses a coarse-grained model for double stranded DNA, cgNA+, to assess nucleosome sequence affinity. cgNA+ coarse-grains DNA on the level of bases and accounts also explicitly for the positions of the backbone phosphates. It has been proven to reproduce all-atom MD data very accurately. It is also ideally suited to be incorporated into a nucleosome model because it is known that DNA is bound to the protein core of the nucleosome via the phosphates.

It is still unclear whether this harmonic model parametrized for unbound DNA is accurate enough to describe DNA inside the nucleosome. Previous models by other authors, using more coarse-grained models of DNA, have been rather successful in predicting base pair sequence dependent nucleosome behavior. This is at least the case as long as DNA shape is concerned whereas assessing the role of DNA bendability (something this paper focuses on) has been consistently challenging in all nucleosome models to my knowledge.

It is thus of major interest whether this more sophisticated model is also more successful in handling this issue. As far as I can tell the work is technically sound and properly accounts for not only the energy required in wrapping DNA but also entropic effects, namely the change in entropy that DNA experiences when going from the free state to the bound state. The authors make an approximation here which seems to me to be a reasonable first step.

Of interest is also that the authors have the parameters at hand to study the effect of methylation of CpG-steps. This is especially interesting as this allows to study a scenario where changes in the physical properties of base pair steps via methylation might influence nucleosome positioning and stability in a cell-type specific way.

Overall, this is an important contribution to the questions of how sequence affects nucleosome positioning and affinity. The findings suggest that cgNA+ has something new to offer. But the problem is complex, also on the experimental side, so many questions remain open. Despite of this, I highly recommend publication of this manuscript.

Strengths:

The authors use their state-of-the-art coarse grained DNA model which seems ideally suited to be applied to nucleosomes as it accounts explicitly for the backbone phosphates.

Weaknesses:

The authors introduce penalty coefficients c_i to avoid steric clashes between the two DNA turns in the nucleosome. This requires c_i-values that are so high that standard deviations in the fluctuations of the simulation are smaller than in the experiments.

Indeed, smaller c_i values lead to steric clashes between the two turns of DNA. A possible improvement of our optimisation method and a direction of future work would be adding a penalty which prevents steric clashes to the objective function. Then the c_i values could be reduced to have bigger fluctuations that are even closer to the experimental structures.

Reviewer #3 (Public Review):

Summary:

In this study, authors utilize biophysical modeling to investigate differences in free energies and nucleosomal configuration probability density of CpG islands and nonmethylated regions in the genome. Toward this goal, they develop and apply the cgNA+ coarse-grained model, an extension of their prior molecular modeling framework.

Strengths:

The study utilizes biophysical modeling to gain mechanistic insight into nucleosomal occupancy differences in CpG and nonmethylated regions in the genome.

Weaknesses:

Although the overall study is interesting, the manuscripts need more clarity in places. Moreover, the rationale and conclusion for some of the analyses are not well described.

We have revised the manuscript in accordance with the reviewer’s latest suggestions.

Comments on revised version:

Authors have attempted to address previously raised concerns.

Reviewer #1 (Recommendations for the authors):

The authors have addressed most of my comments and concerns regarding this manuscript. Among them, the most significant pertains to fitting the coarse-grained model using a different all-atom force field to verify the conclusions. The authors acknowledged this point but noted the computational cost involved and proposed it as a direction for future work. Overall, I recommend the revised version for publication.

Reviewer #2 (Recommendations for the authors):

My previous comments were addressed satisfactorily.

Reviewer #3 (Recommendations for the authors):

Authors have attempted to address previously raised concerns. However, some concerns listed below remain that need to be addressed.

(1) The first reviewer makes a valid point regarding the reconciliation of conflicting observations related to nucleosome-forming affinity and wrapping energy. Unfortunately, the authors don’t seem to address this and state that this will be the goal for the future study.

Training the cgNA+ model on alternative MD simulation datasets remains future work. However, we revised the Discussion section to more clearly address the conflicting experimental findings in the literature on how DNA methylation influences nucleosome formation.

(2) Please report the effect size and statistical significance value for Figures 7 and 8, as this information is currently not provided, despite the authors’ claim that these observations are statistically significant.

This information is now presented in Supplementary Tables S1-S4.

(3) In response to the discrepancy in cell lines for correlating nucleosome occupancy and methylation analyses, the authors claim that there is no publicly available nucleosome occupancy and methylation data for a human cell type within the human genome. This claim is confusing, as the GM12878 cell line has been extensively characterized with MNaseseq and WGBS.

We thank the reviewer for this remark. We have removed the statement regarding the lack of data from the manuscript; we intend to examine the suggested cell line in future research.

(4) In response to my question, the authors claimed that they selected regions from chromosome 1 exclusively; however, the observation remains unchanged when considering sequence samples from different genomic regions. They should provide examples from different chromosomes as part of the supplementary information to further support this.

The examples of corresponding plots for other nucleosomes are now shown in Supplementary Figure S9.

Author response:

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

Reviewer #1 (Public review):

In this manuscript, Domingo et al. present a novel perturbation-based approach to experimentally modulate the dosage of genes in cell lines. Their approach is capable of gradually increasing and decreasing gene expression. The authors then use their approach to perturb three key transcription factors and measure the downstream effects on gene expression. Their analysis of the dosage response curve of downstream genes reveals marked non-linearity.

One of the strengths of this study is that many of the perturbations fall within the physiological range for each cis gene. This range is presumably between a single-copy state of heterozygous loss-of-function (log fold change of -1) and a three-copy state (log fold change of ~0.6). This is in contrast with CRISPRi or CRISPRa studies that attempt to maximize the effect of the perturbation, which may result in downstream effects that are not representative of physiological responses.

Another strength of the study is that various points along the dosage-response curve were assayed for each perturbed gene. This allowed the authors to effectively characterize the degree of linearity and monotonicity of each dosage-response relationship. Ultimately, the study revealed that many of these relationships are non-linear, and that the response to activation can be dramatically different than the response to inhibition.

To test their ability to gradually modulate dosage, the authors chose to measure three transcription factors and around 80 known downstream targets. As the authors themselves point out in their discussion about MYB, this biased sample of genes makes it unclear how this approach would generalize genome-wide. In addition, the data generated from this small sample of genes may not represent genome-wide patterns of dosage response. Nevertheless, this unique data set and approach represents a first step in understanding dosage-response relationships between genes.

Another point of general concern in such screens is the use of the immortalized K562 cell line. It is unclear how the biology of these cell lines translates to the in vivo biology of primary cells. However, the authors do follow up with cell-type-specific analyses (Figures 4B, 4C, and 5A) to draw a correspondence between their perturbation results and the relevant biology in primary cells and complex diseases.

The conclusions of the study are generally well supported with statistical analysis throughout the manuscript. As an example, the authors utilize well-known model selection methods to identify when there was evidence for non-linear dosage response relationships.

Gradual modulation of gene dosage is a useful approach to model physiological variation in dosage. Experimental perturbation screens that use CRISPR inhibition or activation often use guide RNAs targeting the transcription start site to maximize their effect on gene expression. Generating a physiological range of variation will allow others to better model physiological conditions.

There is broad interest in the field to identify gene regulatory networks using experimental perturbation approaches. The data from this study provides a good resource for such analytical approaches, especially since both inhibition and activation were tested. In addition, these data provide a nuanced, continuous representation of the relationship between effectors and downstream targets, which may play a role in the development of more rigorous regulatory networks.

Human geneticists often focus on loss-of-function variants, which represent natural knock-down experiments, to determine the role of a gene in the biology of a trait. This study demonstrates that dosage response relationships are often non-linear, meaning that the effect of a loss-of-function variant may not necessarily carry information about increases in gene dosage. For the field, this implies that others should continue to focus on both inhibition and activation to fully characterize the relationship between gene and trait.

We thank the reviewer for their thoughtful and thorough evaluation of our study. We appreciate their recognition of the strengths of our approach, particularly the ability to modulate gene dosage within a physiological range and to capture non-linear dosage-response relationships. We also agree with the reviewer’s points regarding the limitations of gene selection and the use of K562 cells, and we are encouraged that the reviewer found our follow-up analyses and statistical framework to be well-supported. We believe this work provides a valuable foundation for future genome-wide applications and more physiologically relevant perturbation studies.

Reviewer #2 (Public review):

Summary:

This work investigates transcriptional responses to varying levels of transcription factors (TFs). The authors aim for gradual up- and down-regulation of three transcription factors GFI1B, NFE2, and MYB in K562 cells, by using a CRISPRa- and a CRISPRi line, together with sgRNAs of varying potency. Targeted single-cell RNA sequencing is then used to measure gene expression of a set of 90 genes, which were previously shown to be downstream of GFI1B and NFE2 regulation. This is followed by an extensive computational analysis of the scRNA-seq dataset. By grouping cells with the same perturbations, the authors can obtain groups of cells with varying average TF expression levels. The achieved perturbations are generally subtle, not reaching half or double doses for most samples, and up-regulation is generally weak below 1.5-fold in most cases. Even in this small range, many target genes exhibit a non-linear response. Since this is rather unexpected, it is crucial to rule out technical reasons for these observations.

We thank the reviewer for their detailed and thoughtful assessment of our work. We are encouraged by their recognition of the strengths of our study, including the value of quantitative CRISPR-based perturbation coupled with single-cell transcriptomics, and its potential to inform gene regulatory network inference. Below, we address each of the concerns raised:

Strengths:

The work showcases how a single dataset of CRISPRi/a perturbations with scRNA-seq readout and an extended computational analysis can be used to estimate transcriptome dose responses, a general approach that likely can be built upon in the future.

Weaknesses:

(1) The experiment was only performed in a single replicate. In the absence of an independent validation of the main findings, the robustness of the observations remains unclear.

We acknowledge that our study was performed in a single pooled experiment. While additional replicates would certainly strengthen the findings, in high-throughput single-cell CRISPR screens, individual cells with the same perturbation serve as effective internal replicates. This is a common practice in the field. Nevertheless, we agree that biological replicates would help control for broader technical or environmental effects.

(2) The analysis is based on the calculation of log-fold changes between groups of single cells with non-targeting controls and those carrying a guide RNA driving a specific knockdown. How the fold changes were calculated exactly remains unclear, since it is only stated that the FindMarkers function from the Seurat package was used, which is likely not optimal for quantitative estimates. Furthermore, differential gene expression analysis of scRNA-seq data can suffer from data distortion and mis-estimations (Heumos et al. 2023 (https://doi.org/10.1038/s41576-023-00586-w), Nguyen et al. 2023 (https://doi.org/10.1038/s41467-023-37126-3)). In general, the pseudo-bulk approach used is suitable, but the correct treatment of drop-outs in the scRNA-seq analysis is essential.

We thank the reviewer for highlighting recent concerns in the field. A study benchmarking association testing methods for perturb-seq data found that among existing methods, Seurat’s FindMarkers function performed the best (T. Barry et al. 2024).

In the revised Methods, we now specify the formula used to calculate fold change and clarify that the estimates are derived from the Wilcoxon test implemented in Seurat’s FindMarkers function. We also employed pseudo-bulk grouping to mitigate single-cell noise and dropout effects.

(3) Two different cell lines are used to construct dose-response curves, where a CRISPRi line allows gene down-regulation and the CRISPRa line allows gene upregulation. Although both lines are derived from the same parental line (K562) the expression analysis of Tet2, which is absent in the CRISPRi line, but expressed in the CRISPRa line (Figure S3A) suggests substantial clonal differences between the two lines. Similarly, the PCA in S4A suggests strong batch effects between the two lines. These might confound this analysis.

We agree that baseline differences between CRISPRi and CRISPRa lines could introduce confounding effects if not appropriately controlled for. We emphasize that all comparisons are made as fold changes relative to non-targeting control (NTC) cells within each line, thereby controlling for batch- and clone-specific baseline expression. See figures S4A and S4B.

(4) The study uses pseudo-bulk analysis to estimate the relationship between TF dose and target gene expression. This requires a system that allows quantitative changes in TF expression. The data provided does not convincingly show that this condition is met, which however is an essential prerequisite for the presented conclusions. Specifically, the data shown in Figure S3A shows that upon stronger knock-down, a subpopulation of cells appears, where the targeted TF is not detected anymore (drop-outs). Also Figure 3B (top) suggests that the knock-down is either subtle (similar to NTCs) or strong, but intermediate knock-down (log2-FC of 0.5-1) does not occur. Although the authors argue that this is a technical effect of the scRNA-seq protocol, it is also possible that this represents a binary behavior of the CRISPRi system. Previous work has shown that CRISPRi systems with the KRAB domain largely result in binary repression and not in gradual down-regulation as suggested in this study (Bintu et al. 2016 (https://doi.org/10.1126/science.aab2956), Noviello et al. 2023 (https://doi.org/10.1038/s41467-023-38909-4)).

Figure S3A shows normalized expression values, not fold changes. A pseudobulk approach reduces single-cell noise and dropout effects. To test whether dropout events reflect true binary repression or technical effects, we compared trans-effects across cells with zero versus low-but-detectable target gene expression (Figure S3B). These effects were highly concordant, supporting the interpretation that dropout is largely technical in origin. We agree that KRAB-based repression can exhibit binary behavior in some contexts, but our data suggest that cells with intermediate repression exist and are biologically meaningful. In ongoing unpublished work, we pursue further analysis of these data at the single cell level, and show that for nearly all guides the dosage effects are indeed gradual rather than driven by binary effects across cells.

(5) One of the major conclusions of the study is that non-linear behavior is common. This is not surprising for gene up-regulation, since gene expression will reach a plateau at some point, but it is surprising to be observed for many genes upon TF down-regulation. Specifically, here the target gene responds to a small reduction of TF dose but shows the same response to a stronger knock-down. It would be essential to show that his observation does not arise from the technical concerns described in the previous point and it would require independent experimental validations.

This phenomenon—where relatively small changes in cis gene dosage can exceed the magnitude of cis gene perturbations—is not unique to our study. This also makes biological sense, since transcription factors are known to be highly dosage sensitive and generally show a smaller range of variation than many other genes (that are regulated by TFs). Empirically, these effects have been observed in previous CRISPR perturbation screens conducted in K562 cells, including those by Morris et al. (2023), Gasperini et al. (2019), and Replogle et al. (2022), to name but a few studies that our lab has personally examined the data of.

(6) One of the conclusions of the study is that guide tiling is superior to other methods such as sgRNA mismatches. However, the comparison is unfair, since different numbers of guides are used in the different approaches. Relatedly, the authors point out that tiling sometimes surpassed the effects of TSS-targeting sgRNAs, however, this was the least fair comparison (2 TSS vs 10 tiling guides) and additionally depends on the accurate annotation of TSS in the relevant cell line.

We do not draw this conclusion simply from observing the range achieved but from a more holistic observation. We would like to clarify that the number of sgRNAs used in each approach is proportional to the number of base pairs that can be targeted in each region: while the TSS-targeting strategy is typically constrained to a small window of a few dozen base pairs, tiling covers multiple kilobases upstream and downstream, resulting in more guides by design rather than by experimental bias. The guides with mismatches do not have a great performance for gradual upregulation.

We would also like to point out that the observation that the strongest effects can arise from regions outside the annotated TSS is not unique to our study and has been demonstrated in prior work (referenced in the text).

To address this concern, we have revised the text to clarify that we do not consider guide tiling to be inherently superior to other approaches such as sgRNA mismatches. Rather, we now describe tiling as a practical and straightforward strategy to obtain a wide range of gene dosage effects without requiring prior knowledge beyond the approximate location of the TSS. We believe this rephrasing more accurately reflects the intent and scope of our comparison.

(7) Did the authors achieve their aims? Do the results support the conclusions?: Some of the most important conclusions are not well supported because they rely on accurately determining the quantitative responses of trans genes, which suffers from the previously mentioned concerns.

We appreciate the reviewer’s concern, but we would have wished for a more detailed characterization of which conclusions are not supported, given that we believe our approach actually accounts for the major concerns raised above. We believe that the observation of non-linear effects is a robust conclusion that is also consistent with known biology, with this paper introducing new ways to analyze this phenomenon.

(8) Discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:

Together with other recent publications, this work emphasizes the need to study transcription factor function with quantitative perturbations. Missing documentation of the computational code repository reduces the utility of the methods and data significantly.

Documentation is included as inline comments within the R code files to guide users through the analysis workflow.

Reviewer #1 (Recommendations for the authors):

In Figure 3C (and similar plots of dosage response curves throughout the manuscript), we initially misinterpreted the plots because we assumed that the zero log fold change on the horizontal axis was in the middle of the plot. This gives the incorrect interpretation that the trans genes are insensitive to loss of GFI1B in Figure 3C, for instance. We think it may be helpful to add a line to mark the zero log fold change point, as was done in Figure 3A.

We thank the reviewer for this helpful suggestion. To improve clarity, we have added a vertical line marking the zero log fold change point in Figure 3C and all similar dosage-response plots. We agree this makes the plots easier to interpret at a glance.

Similarly, for heatmaps in the style of Figure 3B, it may be nice to have a column for the non-targeting controls, which should be a white column between the perturbations that increase versus decrease GFI1B.

We appreciate the suggestion. However, because all perturbation effects are computed relative to the non-targeting control (NTC) cells, explicitly including a separate column for NTC in the heatmap would add limited interpretive value and could unnecessarily clutter the figure. For clarity, we have emphasized in the figure legend that the fold changes are relative to the NTC baseline.

We found it challenging to assess the degree of uncertainty in the estimation of log fold changes throughout the paper. For example, the authors state the following on line 190: "We observed substantial differences in the effects of the same guide on the CRISPRi and CRISPRa backgrounds, with no significant correlation between cis gene fold-changes." This claim was challenging to assess because there are no horizontal or vertical error bars on any of the points in Figure 2A. If the log fold change estimates are very noisy, the data could be consistent with noisy observations of a correlated underlying process. Similarly, to our understanding, the dosage response curves are fit assuming that the cis log fold changes are fixed. If there is excessive noise in the estimation of these log fold changes, it may bias the estimated curves. It may be helpful to give an idea of the amount of estimation error in the cis log fold changes.

We agree that assessing the uncertainty in log fold change estimates is important for interpreting both the lack of correlation between CRISPRi and CRISPRa effects (Figure 2A) and the robustness of the dosage-response modeling.

In response, we have now updated Figure 2A to include both vertical and horizontal error bars, representing the standard errors of the log2 fold-change estimates for each guide in the CRISPRi and CRISPRa conditions. These error estimates were computed based on the differential expression analysis performed using the FindMarkers function in Seurat, which models gene expression differences between perturbed and control cells. We also now clarify this in the figure legend and methods.

The authors mention hierarchical clustering on line 313, which identified six clusters. Although a dendrogram is provided, these clusters are not displayed in Figure 4A. We recommend displaying these clusters alongside the dendrogram.

We have added colored bars indicating the clusters to improve the clarity. Thank you for the suggestion.

In Figures 4B and 4C, it was not immediately clear what some of the gene annotations meant. For example, neither the text nor the figure legend discusses what "WBCs", "Platelets", "RBCs", or "Reticulocytes" mean. It would be helpful to include this somewhere other than only the methods to make the figure more clear.

To improve clarity, we have updated the figure legends for Figures 4B and 4C to explicitly define these abbreviations.

We struggled to interpret Figure 4E. Although the authors focus on the association of MYB with pHaplo, we would have appreciated some general discussion about the pattern of associations seen in the figure and what the authors expected to observe.

We have changed the paragraph to add more exposition and clarification:

“The link between selective constraint and response properties is most apparent in the MYB trans network. Specifically, the probability of haploinsufficiency (pHaplo) shows a significant negative correlation with the dynamic range of transcriptional responses (Figure 4G): genes under stronger constraint (higher pHaplo) display smaller dynamic ranges, indicating that dosage-sensitive genes are more tightly buffered against changes in MYB levels. This pattern was not reproduced in the other trans networks (Figure 4E)”.

Line 71: potentially incorrect use of "rending" and incorrect sentence grammar.

Fixed

Line 123: "co-expression correlation across co-expression clusters" - authors may not have intended to use "co-expression" twice.

Original sentence was correct.

Line 246: "correlations" is used twice in "correlations gene-specific correlations."

Fixed.

Reviewer #2 (Recommendations for the authors):

(1) To show that the approach indeed allows gradual down-regulation it would be important to quantify the know-down strength with a single-cell readout for a subset of sgRNAs individually (e.g. flowfish/protein staining flow cytometry).

We agree that single-cell validation of knockdown strength using orthogonal approaches such as flowFISH or protein staining would provide additional support. However, such experiments fall outside the scope of the current study and are not feasible at this stage. We note that the observed transcriptomic changes and dosage responses across multiple perturbations are consistent with effective and graded modulation of gene expression.

(2) Similarly, an independent validation of the observed dose-response relationships, e.g. with individual sgRNAs, can be helpful to support the conclusions about non-linear responses.

Fig. S4C includes replication of trans-effects for a handful of guides used both in this study and in Morris et al. While further orthogonal validation of dose-response relationships would be valuable, such extensive additional work is not currently feasible within the scope of this study. Nonetheless, the high degree of replication in Fig. S4C as well as consistency of patterns observed across multiple sgRNAs and target genes provides strong support for the conclusions drawn from our high-throughput screen.

(3) The calculation of the log2 fold changes should be documented more precisely. To perform a pseudo-bulk analysis, the raw UMI counts should be summed up in each group (NTC, individual targeting sgRNAs), including zero counts, then the data should be normalized and the fold change should be calculated. The DESeq package for example would be useful here.

We have updated the methods in the manuscript to provide more exposition of how the logFC was calculated:

“In our differential expression (DE) analysis, we used Seurat’s FindMarkers() function, which computes the log fold change as the difference between the average normalized gene expression in each group on the natural log scale:

Logfc = log_e(mean(expression in group 1)) - log_e(mean(expression in group 2))

This is calculated in pseudobulk where cells with the same sgRNA are grouped together and the mean expression is compared to the mean expression of cells harbouring NTC guides. To calculate per-gene differential expression p-value between the two cell groups (cells with sgRNA vs cells with NTC), Wilcoxon Rank-Sum test was used”.

(4) A more careful characterization of the cell lines used would be helpful. First, it would be useful to include the quality controls performed when the clonal lines were selected, in the manuscript. Moreover, a transcriptome analysis in comparison to the parental cell line could be performed to show that the cell lines are comparable. In addition, it could be helpful to perform the analysis of the samples separately to see how many of the response behaviors would still be observed.

Details of the quality control steps used during the selection of the CRISPRa clonal line are already included in the Methods section, and Fig. S4A shows the transcriptome comparison of CRISPRi and CRISPRa lines also for non-targeting guides. Regarding the transcriptomic comparison with the parental cell line, we agree that such an analysis would be informative; however, this would require additional experiments that are not feasible within the scope of the current study. Finally, while analyzing the samples separately could provide further insight into response heterogeneity, we focused on identifying robust patterns across perturbations that are reproducible in our pooled screening framework. We believe these aggregate analyses capture the major response behaviors and support the conclusions drawn.

(5) In general we were surprised to see such strong responses in some of the trans genes, in some cases exceeding the fold changes of the cis gene perturbation more than 2x, even at the relatively modest cis gene perturbations (Figures S5-S8). How can this be explained?

This phenomenon—where trans gene responses can exceed the magnitude of cis gene perturbations—is not unique to our study. Similar effects have been observed in previous CRISPR perturbation screens conducted in K562 cells, including those by Morris et al. (2023), Gasperini et al. (2019), and Replogle et al. (2022).

Several factors may contribute to this pattern. One possibility is that certain trans genes are highly sensitive to transcription factor dosage, and therefore exhibit amplified expression changes in response to relatively modest upstream perturbations. Transcription factors are known to be highly dosage sensitive and generally show a smaller range of variation than many other genes (that are regulated by TFs). Mechanistically, this may involve non-linear signal propagation through regulatory networks, in which intermediate regulators or feedback loops amplify the downstream transcriptional response. While our dataset cannot fully disentangle these indirect effects, the consistency of this observation across multiple studies suggests it is a common feature of transcriptional regulation in K562 cells.

(6) In the analysis shown in Figure S3B, the correlation between cells with zero count and >0 counts for the cis gene is calculated. For comparison, this analysis should also show the correlation between the cells with similar cis-gene expression and between truly different populations (e.g. NTC vs strong sgRNA).

The intent of Figure S3B was not to compare biologically distinct populations or perform differential expression analyses—which we have already conducted and reported elsewhere in the manuscript—but rather to assess whether fold change estimates could be biased by differences in the baseline expression of the target gene across individual cells. Specifically, we sought to determine whether cells with zero versus non-zero expression (as can result from dropouts or binary on/off repression from the KRAB-based CRISPRi system) exhibit systematic differences that could distort fold change estimation. As such, the comparisons suggested by the reviewer do not directly relate to the goal of the analysis which Figure S3B was intended to show.

(7) It is unclear why the correlation between different lanes is assessed as quality control metrics in Figure S1C. This does not substitute for replicates.

The intent of Figure S1C was not to serve as a general quality control metric, but rather to illustrate that the targeted transcript capture approach yielded consistent and specific signal across lanes. We acknowledge that this may have been unclear and have revised the relevant sentence in the text to avoid misinterpretation.

“We used the protein hashes and the dCas9 cDNA (indicating the presence or absence of the KRAB domain) to demultiplex and determine the cell line—CRISPRi or CRISPRa. Cells containing a single sgRNA were identified using a Gaussian mixture model (see Methods). Standard quality control procedures were applied to the scRNA-seq data (see Methods). To confirm that the targeted transcript capture approach worked as intended, we assessed concordance across capture lanes (Figure S1C)”.

(8) Figures and legends often miss important information. Figure 3B and S5-S8: what do the transparent bars represent? Figure S1A: color bar label missing. Figure S4D: what are the lines?, Figure S9A: what is the red line? In Figure S8 some of the fitted curves do not overlap with the data points, e.g. PKM. Fig. 2C: why are there more than 96 guide RNAs (see y-axis)?

We have addressed each point as follows:

Figure 3B: The figure legend has been updated to clarify the meaning of the transparent bars.

Figures S5–S8: There are no transparent bars in these figures; we confirmed this in the source plots.

Figure S1A: The color bar label is already described in the figure legend, but we have reformulated the caption text to make this clearer.

Figure S4D: The dashed line represents a linear regression between the x and y variables. The figure caption has been updated accordingly.

Figure S9A: We clarified that the red line shows the median ∆AIC across all genes and conditions.

Figure S8: We agree that some fitted curves (e.g., PKM) do not closely follow the data points. This reflects high noise in these specific measurements; as noted in the text, TET2 is not expected to exert strong trans effects in this context.

Figure 2C: Thank you for catching this. The y-axis numbers were incorrect because the figure displays the proportion of guides (summing to 100%), not raw counts. We have corrected the y-axis label and updated the numbers in the figure to resolve this inconsistency.

(9) The code is deposited on Github, but documentation is missing.

Documentation is included as inline comments within the R code files to guide users through the analysis workflow.

(10) The methods miss a list of sgRNA target sequences.

We thank the reviewer for this observation. A complete table containing all processed data, including the sequences of the sgRNAs used in this study, is available at the following GEO link:

https://www.ncbi.nlm.nih.gov/geo/download/?acc=GSE257547&format=file&file=GSE257547%5Fd2n%5Fprocessed%5Fdata%2Etxt%2Egz

(11) In some parts, the language could be more specific and/or the readability improved, for example:

Line 88: "quantitative landscape".

Changed to “quantitative patterns”.

Lines 88-91: long sentence hard to read.

This complex sentence was broken up into two simpler ones:

“We uncovered quantitative patterns of how gradual changes in transcription dosage lead to linear and non-linear responses in downstream genes. Many downstream genes are associated with rare and complex diseases, with potential effects on cellular phenotypes”.

Line 110: "tiling sgRNAs +/- 1000 bp from the TSS", could maybe be specified by adding that the average distance was around 100 or 110 bps?

Lines 244-246: hard to understand.

We struggle to see the issue here and are not sure how it can be reworded.

Lines 339-342: hard to understand.

These sentences have been reworded to provide more clarity.

(12) A number of typos, and errors are found in the manuscript:

Line 71: "SOX2" -> "SOX9".

FIXED

Line 73: "rending" -> maybe "raising" or "posing"?

FIXED

Line 157: "biassed".

FIXED

Line 245: "exhibited correlations gene-specific correlations with".

FIXED

Multiple instances, e.g. 261: "transgene" -> "trans gene".

FIXED

Line 332: "not reproduced with among the other".

FIXED

Figure S11: betweenness.

This is the correct spelling

There are more typos that we didn't list here.

We went through the manuscript and corrected all the spelling errors and typos.

Author response:

Reviewer #1:

We appreciate the reviewer’s positive assessment of TSvelo and their helpful technical comments. In the revised manuscript, we will:

(1) Provide a clearer discussion of TF–target annotations, their limitations, and potential integration of additional databases.

(2) Clarify the rationale for example-gene selection (e.g., in Fig. 2d).

(3) Re-evaluate and temper the interpretation regarding ANXA4 and early-stage cell-cycle transitions.

(4) Add appropriate references supporting neuronal inside-out migration.

(5) Include additional analysis comparing TF-based transcription rate estimation with ATAC-based estimates from MultiVelo.

(6) Clarify how lineages were determined in Fig. 6g and incorporate barcode-based validation where applicable.

(7) Correct all typographical errors noted.

Reviewer #2:

We appreciate the reviewer’s careful examination of modeling, benchmarking, and interpretation. To address these concerns, we will:

(1) Expand the methodological justification for initial-state selection, add simulations with ground truth, and evaluate U-to-S delay more broadly across genes.

(2) Clarify matrix formulations and ensure consistency in notation (e.g., Eq. 8).

(3) Assess robustness to prior-knowledge graphs and evaluate alternatives beyond ENCODE/ChEA.

(4) Add methodological details on parameter search.

(5) Improve benchmarking on pancreatic endocrine datasets by including clear definitions of velocity pseudotime, ARI for cell-type separation, quantitative evaluation of phase-portrait fits, and appropriate interpretation of consistency metrics for multi-lineage systems.

(6) Reframe claims about “accurate” or “correct” predictions where evidence is qualitative and strengthen quantitative support where possible.

(8) Clarify lineage segmentation and merging when applying PAGA-guided multi-lineage modeling.

Reviewer #3:

We thank the reviewer for highlighting the need for more rigorous benchmarking and conceptual clarity. In response, we will:

(1) Conduct an expanded simulation study incorporating different data-generating models.

(2) Revise all strong claims to more cautious, evidence-based language.

(3) Add a concise table summarizing conceptual and computational differences among RNA-velocity frameworks.

(4) More clearly articulate the conceptual novelty of TSvelo relative to existing approaches.

(5) Include runtime and memory benchmarks across representative datasets.

(6) Explore additional methods in conceptual comparisons and benchmarking analyses.We appreciate the reviewers’ thoughtful input and agree that the suggested analyses and clarifications will significantly improve the rigor and clarity of the manuscript. We will incorporate all recommended revisions in the resubmission and provide a full, detailed, point-by-point response at that time.

Author response:

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

Reviewer #1 (Public review):

(1) The methods section is overly brief. Even if techniques are cited, more experimental details should be included. For example, since the study focuses heavily on methodology, details such as the number of PCR cycles in RT-PCR or the rationale for choosing HA and PB2 as representative in vitro transcripts should be provided.

We thank the reviewer for this important suggestion. We have now expanded the Methods section to include the number of PCR cycles used in RT-PCR (line 407) and have explained the rationale for choosing HA and PB2 as representative transcripts (line 388).

(2) Information on library preparation and sequencing metrics should be included. For example, the total number of reads, any filtering steps, and quality score distributions/cutoff for the analyzed reads.

We agree and have added detailed information on library preparation, filtering criteria, quality score thresholds, and sequencing statistics for each sample (line 422, Figure S2).

(3) In the Results section (line 115, "Quantification of error rate caused by RT"), the mutation rate attributed to viral replication is calculated. However, in line 138, it is unclear whether the reported value reflects PB2, HA, or both, and whether the comparison is based on the error rate of the same viral RNA or the mean of multiple values (as shown in Figure 3A). Please clarify whether this number applies universally to all influenza RNAs or provide the observed range.

We appreciate this point. We have clarified in the Results (line 140) that the reported value corresponds to PB2.

(4) Since the T7 polymerase introduced errors are only applied to the in vitro transcription control, how were these accounted for when comparing mutation rates between transcribed RNA and cell-culture-derived virus?

We agree that errors introduced by T7 RNA polymerase are present only in the in vitro–transcribed RNA control. However, even when taking this into account, the error rate detected in the in vitro transcripts remained substantially lower than that observed in the viral RNA extracted from replicated virus (line 140, Fig.3a). Thus, the difference cannot be explained by T7-derived errors, and our conclusion regarding the elevated mutation rate in cell-culture–derived viral populations remains valid.

(5) Figure 2 shows that a UMI group size of 4 has an error rate of zero, but this group size is not mentioned in the text. Please clarify.

We have revised the Results (line 98) to describe the UMI group size of 4.

Reviewer #2 (Public review):

(1) The application of UMI-based error correction to viral population sequencing has been established in previous studies (e.g., HIV), and this manuscript does not introduce a substantial methodological or conceptual advance beyond its use in the context of influenza.

We appreciate the reviewer’s comment and agree that UMI-based error correction has been applied previously to viral population sequencing, including HIV. However, to our knowledge, relatively few studies have quantitatively evaluated both the performance of this method and the resulting within-quasi-species mutation distributions in detail. In our manuscript, we not only validate the accuracy of UMIbased error correction in the context of influenza virus sequencing, but also quantitatively characterize the features of intra-quasi-species distributions, which provides new insights into the mutational landscape and evolutionary dynamics specific to influenza. We therefore believe that our work goes beyond a simple application of an established method.

(2) The study lacks independent biological replicates or additional viral systems that would strengthen the generalizability of the conclusions.

We agree with the reviewer that the lack of independent biological replicates and additional viral systems limits the generalizability of our findings. In this study, we intentionally focused on single-particle–derived populations of influenza virus to establish a proof-of-principle for our sequencing and analytical framework. While this design provided a clear demonstration of the method’s ability to capture mutation distributions at the single-particle level, we acknowledge that additional biological replicates and testing across diverse viral systems would be necessary to confirm the broader applicability of our observations. Importantly, even within this limited framework, our analysis enabled us to draw conclusions at the level of individual viral populations and to suggest the possibility of comparing their mutation distributions with known evolvability. This highlights the potential of our approach to bridge observations from single particles with broader patterns of viral evolution. In future work, we plan to expand the number of populations analyzed and include additional viral systems, which will allow us to more rigorously assess reproducibility and to establish systematic links between mutation accumulation at the single-particle level and evolutionary dynamics across viruses.

(3) Potential sources of technical error are not explored or explicitly controlled. Key methodological details are missing, including the number of PCR cycles, the input number of molecules, and UMI family size distributions.

We thank the reviewer for this important suggestion. We have now expanded the Methods section to include the number of PCR cycles used in RT-PCR (line 407). In addition, we have added information on the estimated number of input molecules. Regarding the UMI family size distributions, we have added the data as Figure S2 and referred to it in the revised manuscript.

Finally, with respect to potential sources of technical error, we note that this point is already addressed in the manuscript by direct comparison with in vitro transcribed RNA controls, which encompass errors introduced throughout the entire experimental process. This comparison demonstrates that the error-correction strategy employed here effectively reduces the impact of PCR or sequencing artifacts.

(4) The assertion that variants at ≥0.1% frequency can be reliably detected is based on total read count rather than the number of unique input molecules. Without information on UMI diversity and family sizes, the detection limit cannot be reliably assessed.

We thank the reviewer for raising this important issue. We agree that our original description was misleading, as the reliable detection limit should not be defined solely by total read count. In the revised version, we have added information on UMI distribution and family sizes (Figure S2), and we now state the detection limit in terms of consensus reads. Specifically, we define that variants can be reliably detected when ≥10,000 consensus reads are obtained with a group size of ≥3 (line 173). 

(5)  Although genetic variation is described, the functional relevance of observed mutations in HA and NA is not addressed or discussed.

We appreciate the reviewer’s suggestion. In our study, we did not apply drug or immune selection pressure; therefore, we did not expect to detect mutations that are already known to cause major antigenic changes in HA or NA, and we think it is difficult to discuss such functional implications in this context. However, as noted in discussion, we did identify drug resistance–associated mutations. This observation suggests that the quasi-species pool may provide functional variation, including resistance, even in the absence of explicit selective pressure. We have clarified this point in the text to better address the reviewer’s concern (line 330).

(6) The experimental scale is small, with only four viral populations derived from single particles analyzed. This limited sample size restricts the ability to draw broader conclusions.

We thank the reviewer for pointing out the limitation of analyzing only four viral populations derived from single particles. We fully acknowledge that the small sample size restricts the generalizability of our conclusions. Nevertheless, we would like to emphasize that even within this limited dataset, our results consistently revealed a slight but reproducible deviation of the mutation distribution from the Poisson expectation, as well as a weak correlation with inter-strain conservation. These recurring patterns highlight the robustness of our observations despite the sample size.

In future work, we plan to expand the number of viral populations analyzed and to monitor mutation distributions during serial passage under defined selective pressures. We believe that such expanded analyses will enable us to more reliably assess how mutations accumulate and to develop predictive frameworks for viral evolution.

Reviewer #1 (Recommendations for the authors):

(1)  Please mention Figure 1 and S2 in the text.

Done. We now explicitly reference Figures 1 and S2 (renamed to S1 according to appearance order) in the appropriate sections (lines 74, 124).

(2)  In Figure 4A, please specify which graph corresponds to PB2 and which to PB2-like sequences.

Corrected. Figure 4A legend now specify PB2 vs. PB2-like sequences.

(3)  Consider reducing redundancy in lines 74, 149, 170, 214, and 215.

We thank the reviewer for this stylistic suggestion. We have revised the text to reduce redundancy in these lines.

Reviewer #2 (Recommendations for the authors):

(1)  The manuscript states that "with 10,000 sequencing reads per gene ...variants at ≥0.1% frequency can be reliably detected." However, this interpretation conflates raw read counts with independent input molecules.

We have revised this statement throughout the text to clarify that sensitivity depends on the number of unique UMIs rather than raw read counts (line 173). To support this, we calculated the probability of detecting a true variant present at a frequency of 0.1% within a population. When sequencing ≥10,000 unique molecules, such a variant would be observed at least twice with a probability of approximately 99.95%. In contrast, the error rate of in vitro–transcribed RNA, reflecting errors introduced during the experimental process, was estimated to be on the order of 10⁻⁶ (line 140, Fig. 3a). Under this condition, the probability that the same artificial error would arise independently at the same position in two out of 10,000 molecules is <0.5%. Therefore, variants present at ≥0.1% can be reliably distinguished from technical artifacts and are confidently detected under our sequencing conditions.

(2) To support the claimed sensitivity, please provide for each gene and population: (a) UMI family size distributions, (b) number of PCR cycles and input molecule counts, and (c) recalculation of the detection limit based on unique molecules.

If possible, I encourage experimental validation of sensitivity claims, such as spike-in controls at known variant frequencies, dilution series, or technical replicates to demonstrate reproducibility at the 0.1% detection level.

We have added (a) histograms of UMI family size distributions for each gene and population (Figure S2), (b) detailed method RT-PCR protocol and estimated input counts (line 407), and (c) recalculated detection limits (line 173).

We appreciate the reviewer’s suggestion and fully recognize the value of spike-in experiments. However, given the observed mutation rate of T7-derived RNA and the sufficient sequencing depth in our dataset, it is evident that variants above the 0.1% threshold can be robustly detected without additional spike-in controls.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

The aim of this paper is to develop a simple method to quantify fluctuations in the partitioning of cellular elements. In particular, they propose a flow-cytometry based method coupled with a simple mathematical theory as an alternative to conventional imaging-based approaches.

Strengths:

The approach they develop is simple to understand and its use with flow-cytometry measurements is clearly explained. Understanding how the fluctuations in the cytoplasm partition varies for different kinds of cells is particularly interesting.

Weaknesses:

The theory only considers fluctuations due to cellular division events. Fluctuations in cellular components are largely affected by various intrinsic and extrinsic sources of noise and only under particular conditions does partitioning noise become the dominant source of noise. In the revised version of the manuscript, they argue that in their setup, noise due to production and degradation processes are negligible but noise due to extrinsic sources such as those stemming from cell-cycle length variability may still be important. To investigate the robustness of their modelling approach to such noise, they simulated cells following a sizer-like division strategy, a scenario that maximizes the coupling between fluctuations in cell-division time and partitioning noise. They find that estimates remain within the pre-established experimental error margin.

We thank the Reviewer for her/his work in revising our manuscript.

Reviewer #2 (Public review):

Summary:

The authors present a combined experimental and theoretical workflow to study partitioning noise arising during cell division. Such quantifications usually require time-lapse experiments, which are limited in throughput. To bypass these limitations, the authors propose to use flow-cytometry measurements instead and analyse them using a theoretical model of partitioning noise. The problem considered by the authors is relevant and the idea to use statistical models in combination with flow cytometry to boost statistical power is elegant. The authors demonstrate their approach using experimental flow cytometry measurements and validate their results using time-lapse microscopy. The approach focuses on a particular case, where the dynamics of the labelled component depends predominantly on partitioning, while turnover of components is not taken into account. The description of the methods is significantly clearer than in the previous version of the manuscript.

We thank the Reviewer for her/his work in revising our manuscript. In the following, we address the remaining raised points.

I have only two comments left:

• In eq. (1) the notation has been changed/corrected, but the text immediately after it still refers to the old notation.

We have fixed the notation.

• Maybe I don't fully understand the reasoning provided by the authors, but it is still not entirely clear to me why microscopy-based estimates are expected to be larger. Fewer samples will increase the estimation uncertainty, but this can go either way in terms of the inferred variability.

We thank the Reviewer for giving us the opportunity to clarify this point. In the previous answer, we focused on the role of the gating strategy, highlighting how the limited statistics available with microscopy reduce the chances of a stronger selection of the events. The explanation for why the noise is biased toward increasing the estimation of division asymmetry relies on multiple aspects: First, due to the multiple sources of noise affecting fluorescence intensity, the experimental procedure, and the segmentation protocol, the measurements of the fluorescence intensity of single cells fluctuate. This variability adds to the inherent stochasticity of the partitioning process, thereby increasing the overall variance of the distribution.

To illustrate this effect, we simulated the microscopy data. We extracted a fraction f from a Gaussian distribution with mean µ = 𝑝 and standard deviation σ = σ_{𝑡𝑟𝑢𝑒} , i.e. 𝑁(𝑝, σ_{𝑡𝑟𝑢𝑒}). We then simulated different time frames by adding noise drawn from a Gaussian distribution with mean µ = 0 and standard deviation σ = σ_{𝑛𝑜𝑖𝑠𝑒} , i.e., 𝑁(0, σ_{𝑛𝑜𝑖𝑠𝑒}), to f. An equal process was applied to 1 − f. The added noise was resampled so that the two measurements remained independent. Figure 6 shows a sample dynamic where the empty gray circles represent the true fractions. We then fitted the two dynamics to a linear equation with a common slope and obtained an estimate of the partitioning noise.

By repeating this process a number of times consistent with the experiment, we measured the resulting standard deviation of the new partitioning distribution. Figure 7 shows the distribution of the measured standard deviation over multiple repetitions of the simulations. Each histogram is the variance of the partitioning distribution obtained from 100 simulations of the noisy (and non noisy) fluorescence dynamic. By comparing this with the distribution of the standard deviation of the non-noisy dynamics, it is possible to observe that, on average, the added noise leads to a greater estimated variance. The magnitude of this increase depends on the variance of the added noise, but it is always biased toward larger values.

This represents only one component of the effect. The shown distributions and simulations are intended solely to demonstrate the direction of the bias, and not to account for the exact difference between the flow cytometry and microscopy estimates. In the proposed case, where noise and true variance are equal, the resulting difference in division asymmetry is 1.3.

A second contribution arises from the segmentation protocol. As we stated, a major limitation of the microscopy-based approach is the need for manual image segmentation. This reduces the amount of available data and introduces potential errors. Even though different checks were applied, some situations are difficult to avoid. For example, when daughter cells are very close to each other, the borders may not be precisely recognized; cells may overlap; or speckles may remain undetected. In all these cases, it is easier to overestimate the fluorescence than to underestimate it, thereby increasing the chance of an extremal event.

Indeed, segmentation relies on both brightfield and fluorescence images. Errors in defining the cell outline are more likely when fluorescence is low, since borders, overlaps, and speckles are more evident against a darker background. This introduces an additional bias toward higher asymmetry, increasing the number of events in the tail of the partitioning distribution.

Both aspects described above could be mitigated by increasing the available statistics. In particular, by applying stricter selection criteria, such as imposing limits on fluorescence intensity fluctuations, the distribution should approach the expected one.

A similar issue does not arise in flow cytometry experiments. From the initial sorting procedure, which ensures a cleaner separation of peaks, to the morphological checks performed at each acquisition point, the availability of a large number of measured events reduces both measurement noise and segmentation errors.

A discussion on these aspects has been added in the revised version of the Supplementary Materials and in the Main Text.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, participants completed two different tasks. A perceptual choice task in which they compared the sizes of pairs of items and a value-different task in which they identified the higher value option among pairs of items with the two tasks involving the same stimuli. Based on previous fMRI research, the authors sought to determine whether the superior frontal sulcus (SFS) is involved in both perceptual and value-based decisions or just one or the other. Initial fMRI analyses were devised to isolate brain regions that were activated for both types of choices and also regions that were unique to each. Transcranial magnetic stimulation was applied to the SFS in between fMRI sessions and it was found to lead to a significant decrease in accuracy and RT on the perceptual choice task but only a decrease in RT on the value-different task. Hierarchical drift-diffusion modelling of the data indicated that the TMS had led to a lowering of decision boundaries in the perceptual task and a lower of non-decision times on the value-based task. Additional analyses show that SFS covaries with model-derived estimates of cumulative evidence and that this relationship is weakened by TMS.

Strengths:

The paper has many strengths including the rigorous multi-pronged approach of causal manipulation, fMRI and computational modelling which offers a fresh perspective on the neural drivers of decision making. Some additional strengths include the careful paradigm design which ensured that the two types of tasks were matched for their perceptual content while orthogonalizing trial-to-trial variations in choice difficulty. The paper also lays out a number of specific hypotheses at the outset regarding the behavioural outcomes that are tied to decision model parameters and are well justified.

Weaknesses:

(1.1) Unless I have missed it, the SFS does not actually appear in the list of brain areas significantly activated by the perceptual and value tasks in Supplementary Tables 1 and 2. Its presence or absence from the list of significant activations is not mentioned by the authors when outlining these results in the main text. What are we to make of the fact that it is not showing significant activation in these initial analyses?

You are right that the left SFS does not appear in our initial task-level contrasts. Those first analyses were deliberately agnostic to evidence accumulation (i.e., average BOLD by task, irrespective of trial-by-trial evidence). Consistent with prior work, SFS emerges only when we model the parametric variation in accumulated perceptual evidence.

Accordingly, we ran a second-level GLM that included trial-wise accumulated evidence (aE) as a parametric modulator. In that analysis, the left SFS shows significant aE-related activity specifically during perceptual decisions, but not during value-based decisions (SVC in a 10-mm sphere around x = −24, y = 24, z = 36).

To avoid confusion, we now:

(i) explicitly separate and label the two analysis levels in the Results; (ii) state up front that SFS is not expected to appear in the task-average contrast; and (iii) add a short pointer that SFS appears once aE is included as a parametric modulator. We also edited Methods to spell out precisely how aE is constructed and entered into GLM2. This should make the logic of the two-stage analysis clearer and aligns the manuscript with the literature where SFS typically emerges only in parametric evidence models.

(1.2) The value difference task also requires identification of the stimuli, and therefore perceptual decision-making. In light of this, the initial fMRI analyses do not seem terribly informative for the present purposes as areas that are activated for both types of tasks could conceivably be specifically supporting perceptual decision-making only. I would have thought brain areas that are playing a particular role in evidence accumulation would be best identified based on whether their BOLD response scaled with evidence strength in each condition which would make it more likely that areas particular to each type of choice can be identified. The rationale for the authors' approach could be better justified.

We agree that both tasks require early sensory identification of the items, but the decision-relevant evidence differs by design (size difference vs. value difference), and our modelling is targeted at the evidence integration stage rather than initial identification.

To address your concern empirically, we: (i) added session-wise plots of mean RTs showing a general speed-up across the experiment (now in the Supplement); (ii) fit a hierarchical DDM to jointly explain accuracy and RT. The DDM dissociates decision time (evidence integration) from non-decision time (encoding/response execution).

After cTBS, perceptual decisions show a selective reduction of the decision boundary (lower accuracy, faster RTs; no drift-rate change), whereas value-based decisions show no change to boundary/drift but a decrease in non-decision time, consistent with faster sensorimotor processing or task familiarity. Thus, the TMS effect in SFS is specific to the criterion for perceptual evidence accumulation, while the RT speed-up in the value task reflects decision-irrelevant processes. We now state this explicitly in the Results and add the RT-by-run figure for transparency.

(1.2.1) The value difference task also requires identification of the stimuli, and therefore perceptual decision-making. In light of this, the initial fMRI analyses do not seem terribly informative for the present purposes as areas that are activated for both types of tasks could conceivably be specifically supporting perceptual decision-making only.

Thank you for prompting this clarification.

The key point is what changes with cTBS. If SFS supported generic identification, we would expect parallel cTBS effects on drift rate (or boundary) in both tasks. Instead, we find: (a) boundary decreases selectively in perceptual decisions (consistent with SFS setting the amount of perceptual evidence required), and (b) non-decision time decreases selectively in the value task (consistent with speed-ups in encoding/response stages). Moreover, trial-by-trial SFS BOLD predicts perceptual accuracy (controlling for evidence), and neural-DDM model comparison shows SFS activity modulates boundary, not drift, during perceptual choices.

Together, these converging behavioral, computational, and neural results argue that SFS specifically supports the criterion for perceptual evidence accumulation rather than generic visual identification.

(1.2.2) I would have thought brain areas that are playing a particular role in evidence accumulation would be best identified based on whether their BOLD response scaled with evidence strength in each condition which would make it more likely that areas particular to each type of choice can be identified. The rationale for the authors' approach could be better justified.

We now more explicitly justify the two-level fMRI approach. The task-average contrast addresses which networks are generally more engaged by each domain (e.g., posterior parietal for PDM; vmPFC/PCC for VDM), given identical stimuli and motor outputs. This complements, but does not substitute for, the parametric evidence analysis, which is where one expects accumulation-related regions such as SFS to emerge. We added text clarifying that the first analysis establishes domain-specific recruitment at the task level, whereas the second isolates evidence-dependent signals (aE) and reveals that left SFS tracks accumulated evidence only for perceptual choices. We also added explicit references to the literature using similar two-step logic and noted that SFS typically appears only in parametric evidence models.

(1.3) TMS led to reductions in RT in the value-difference as well as the perceptual choice task. DDM modelling indicated that in the case of the value task, the effect was attributable to reduced non-decision time which the authors attribute to task learning. The reasoning here is a little unclear.

(1.3.1) Comment: If task learning is the cause, then why are similar non-decision time effects not observed in the perceptual choice task?

Great point. The DDM addresses exactly this: RT comprises decision time (DT) plus non-decision time (nDT). With cTBS, PDM shows reduced DT (via a lower boundary) but stable nDT; VDM shows reduced nDT with no change to boundary/drift. Hence, the superficially similar RT speed-ups in both tasks are explained by different latent processes: decision-relevant in PDM (lower criterion → faster decisions, lower accuracy) and decision-irrelevant in VDM (faster encoding/response). We added explicit language and a supplemental figure showing RT across runs, and we clarified in the text that only the PDM speed-up reflects a change to evidence integration.

(1.3.2) Given that the value-task actually requires perceptual decision-making, is it not possible that SFS disruption impacted the speed with which the items could be identified, hence delaying the onset of the value-comparison choice?

We agree there is a brief perceptual encoding phase at the start of both tasks. If cTBS impaired visual identification per se, we would expect longer nDT in both tasks or a decrease in drift rate. Instead, nDT decreases in the value task and is unchanged in the perceptual task; drift is unchanged in both. Thus, cTBS over SFS does not slow identification; rather, it lowers the criterion for perceptual accumulation (PDM) and, separately, we observe faster non-decision components in VDM (likely familiarity or motor preparation). We added a clarifying sentence noting that item identification was easy and highly overlearned (static, large food pictures), and we cite that nDT is the appropriate locus for identification effects in the DDM framework; our data do not show the pattern expected of impaired identification.

(1.4) The sample size is relatively small. The authors state that 20 subjects is 'in the acceptable range' but it is not clear what is meant by this.

We have clarified what we mean and provided citations. The sample (n = 20) matches or exceeds many prior causal TMS/fMRI studies targeting perceptual decision circuitry (e.g., Philiastides et al., 2011; Rahnev et al., 2016; Jackson et al., 2021; van der Plas et al., 2021; Murd et al., 2021). Importantly, we (i) use within-subject, pre/post cTBS differences-in-differences with matched tasks; (ii) estimate hierarchical models that borrow strength across participants; and (iii) converge across behavior, latent parameters, regional BOLD, and connectivity. We now replace the vague phrase with a concrete statement and references, and we report precision (HDIs/SEs) for all main effects.

Reviewer #2 (Public Review):

Summary:

The authors set out to test whether a TMS-induced reduction in excitability of the left Superior Frontal Sulcus influenced evidence integration in perceptual and value-based decisions. They directly compared behaviour - including fits to a computational decision process model - and fMRI pre and post-TMS in one of each type of decision-making task. Their goal was to test domain-specific theories of the prefrontal cortex by examining whether the proposed role of the SFS in evidence integration was selective for perceptual but not value-based evidence.

Strengths:

The paper presents multiple credible sources of evidence for the role of the left SFS in perceptual decision-making, finding similar mechanisms to prior literature and a nuanced discussion of where they diverge from prior findings. The value-based and perceptual decision-making tasks were carefully matched in terms of stimulus display and motor response, making their comparison credible.

Weaknesses:

(2.1) More information on the task and details of the behavioural modelling would be helpful for interpreting the results.

Thank you for this request for clarity. In the revision we explicitly state, up front, how the two tasks differ and how the modelling maps onto those differences.

(1) Task separability and “evidence.” We now define task-relevant evidence as size difference (SD) for perceptual decisions (PDM) and value difference (VD) for value-based decisions (VDM). Stimuli and motor mappings are identical across tasks; only the evidence to be integrated changes.

(2) Behavioural separability that mirrors task design. As reported, mixed-effects regressions show PDM accuracy increases with SD (β=0.560, p<0.001) but not VD (β=0.023, p=0.178), and PDM RTs shorten with SD (β=−0.057, p<0.001) but not VD (β=0.002, p=0.281). Conversely, VDM accuracy increases with VD (β=0.249, p<0.001) but not SD (β=0.005, p=0.826), and VDM RTs shorten with VD (β=−0.016, p=0.011) but not SD (β=−0.003, p=0.419).

(3 How the HDDM reflects this. The hierarchical DDM fits the joint accuracy–RT distributions with task-specific evidence (SD or VD) as the predictor of drift. The model separates decision time from non-decision time (nDT), which is essential for interpreting the different RT patterns across tasks without assuming differences in the accumulation process when accuracy is unchanged.

These clarifications are integrated in the Methods (Experimental paradigm; HDDM) and in Results (“Behaviour: validity of task-relevant pre-requisites” and “Modelling: faster RTs during value-based decisions is related to non-decision-related sensorimotor processes”).

(2.2) The evidence for a choice and 'accuracy' of that choice in both tasks was determined by a rating task that was done in advance of the main testing blocks (twice for each stimulus). For the perceptual decisions, this involved asking participants to quantify a size metric for the stimuli, but the veracity of these ratings was not reported, nor was the consistency of the value-based ones. It is my understanding that the size ratings were used to define the amount of perceptual evidence in a trial, rather than the true size differences, and without seeing more data the reliability of this approach is unclear. More concerning was the effect of 'evidence level' on behaviour in the value-based task (Figure 3a). While the 'proportion correct' increases monotonically with the evidence level for the perceptual decisions, for the value-based task it increases from the lowest evidence level and then appears to plateau at just above 80%. This difference in behaviour between the two tasks brings into question the validity of the DDM which is used to fit the data, which assumes that the drift rate increases linearly in proportion to the level of evidence.

We thank the reviewer for raising these concerns, and we address each of them point by point:

2.2.1. Comment: It is my understanding that the size ratings were used to define the amount of perceptual evidence in a trial, rather than the true size differences, and without seeing more data the reliability of this approach is unclear.

That is correct—we used participants’ area/size ratings to construct perceptual evidence (SD).

To validate this choice, we compared those ratings against an objective image-based size measure (proportion of non-black pixels within the bounding box). As shown in Author response image 3, perceptual size ratings are highly correlated with objective size across participants (Pearson r values predominantly ≈0.8 or higher; all p<0.001). Importantly, value ratings do not correlate with objective size (Author response image 2), confirming that the two rating scales capture distinct constructs. These checks support using participants’ size ratings as the participant-specific ground truth for defining SD in the PDM trials.

Author response image 1.

Objective size and value ratings are unrelated. Scatterplots show, for each participant, the correlation between objective image size (x-axis; proportion of non-black pixels within the item box) and value-based ratings (y-axis; 0–100 scale). Each dot is one food item (ratings averaged over the two value-rating repetitions). Across participants, value ratings do not track objective size, confirming that value and size are distinct constructs.

Author response image 2.

Perceptual size ratings closely track objective size. Scatterplots show, for each participant, the correlation between objective image size (x-axis) and perceptual area/size ratings (y-axis; 0–100 scale). Each dot is one food item (ratings averaged over the two perceptual ratings). Perceptual ratings are strongly correlated with objective size for nearly all participants (see main text), validating the use of these ratings to construct size-difference evidence (SD).

(2.2.2) More concerning was the effect of 'evidence level' on behaviour in the value-based task (Figure 3a). While the 'proportion correct' increases monotonically with the evidence level for the perceptual decisions, for the value-based task it increases from the lowest evidence level and then appears to plateau at just above 80%. This difference in behaviour between the two tasks brings into question the validity of the DDM which is used to fit the data, which assumes that the drift rate increases linearly in proportion to the level of evidence.

We agree that accuracy appears to asymptote in VDM, but the DDM fits indicate that the drift rate still increases monotonically with evidence in both tasks. In Supplementary figure 11, drift (δ) rises across the four evidence levels for PDM and for VDM (panels showing all data and pre/post-TMS). The apparent plateau in proportion correct during VDM reflects higher choice variability at stronger preference differences, not a failure of the drift–evidence mapping. Crucially, the model captures both the accuracy patterns and the RT distributions (see posterior predictive checks in Supplementary figures 11-16), indicating that a monotonic evidence–drift relation is sufficient to account for the data in each task.

Author response image 3.

HDDM parameters by evidence level. Group-level posterior means (± posterior SD) for drift (δ), boundary (α), and non-decision time (τ) across the four evidence levels, shown (a) collapsed across TMS sessions, (b) for PDM (blue) pre- vs post-TMS (light vs dark), and (c) for VDM (orange) pre- vs post-TMS. Crucially, drift increases monotonically with evidence in both tasks, while TMS selectively lowers α in PDM and reduces τ in VDM (see Supplementary Tables for numerical estimates).

(2.3) The paper provides very little information on the model fits (no parameter estimates, goodness of fit values or simulated behavioural predictions). The paper finds that TMS reduced the decision bound for perceptual decisions but only affected non-decision time for value-based decisions. It would aid the interpretation of this finding if the relative reliability of the fits for the two tasks was presented.

We appreciate the suggestion and have made the quantitative fit information explicit:

(1) Parameter estimates. Group-level means/SDs for drift (δ), boundary (α), and nDT (τ) are reported for PDM and VDM overall, by evidence level, pre- vs post-TMS, and per subject (see Supplementary Tables 8-11).

(2) Goodness of fit and predictive adequacy. DIC values accompany each fit in the tables. Posterior predictive checks demonstrate close correspondence between simulated and observed accuracy and RT distributions overall, by evidence level, and across subjects (Supplementary Figures 11-16).

Together, these materials document that the HDDM provides reliable fits in both tasks and accurately recovers the qualitative and quantitative patterns that underlie our inferences (reduced α for PDM only; selective τ reduction in VDM).

(2.4) Behaviourally, the perceptual task produced decreased response times and accuracy post-TMS, consistent with a reduced bound and consistent with some prior literature. Based on the results of the computational modelling, the authors conclude that RT differences in the value-based task are due to task-related learning, while those in the perceptual task are 'decision relevant'. It is not fully clear why there would be such significantly greater task-related learning in the value-based task relative to the perceptual one. And if such learning is occurring, could it potentially also tend to increase the consistency of choices, thereby counteracting any possible TMS-induced reduction of consistency?

Thank you for pointing out the need for a clearer framing. We have removed the speculative label “task-related learning” and now describe the pattern strictly in terms of the HDDM decomposition and neural results already reported:

(1) VDM: Post-TMS RTs are faster while accuracy is unchanged. The HDDM attributes this to a selective reduction in non-decision time (τ), with no change in decision-relevant parameters (α, δ) for VDM (see Supplementary Figure 11 and Supplementary Tables). Consistent with this, left SFS BOLD is not reduced for VDM, and trialwise SFS activity does not predict VDM accuracy—both observations argue against a change in VDM decision formation within left SFS.

(2) PDM: Post-TMS accuracy decreases and RTs shorten, which the HDDM captures as a lower decision boundary (α) with no change in drift (δ). Here, left SFS BOLD scales with accumulated evidence and decreases post-TMS, and trialwise SFS activity predicts PDM accuracy, all consistent with a decision-relevant effect in PDM.

Regarding the possibility that faster VDM RTs should increase choice consistency: empirically, consistency did not change in VDM, and the HDDM finds no decision-parameter shifts there. Thus, there is no hidden counteracting increase in VDM accuracy that could mask a TMS effect—the absence of a VDM accuracy change is itself informative and aligns with the modelling and fMRI.

Reviewer #3 (Public Review):

Summary:

Garcia et al., investigated whether the human left superior frontal sulcus (SFS) is involved in integrating evidence for decisions across either perceptual and/or value-based decision-making. Specifically, they had 20 participants perform two decision-making tasks (with matched stimuli and motor responses) in an fMRI scanner both before and after they received continuous theta burst transcranial magnetic stimulation (TMS) of the left SFS. The stimulation thought to decrease neural activity in the targeted region, led to reduced accuracy on the perceptual decision task only. The pattern of results across both model-free and model-based (Drift diffusion model) behavioural and fMRI analyses suggests that the left SLS plays a critical role in perceptual decisions only, with no equivalent effects found for value-based decisions. The DDM-based analyses revealed that the role of the left SLS in perceptual evidence accumulation is likely to be one of decision boundary setting. Hence the authors conclude that the left SFS plays a domain-specific causal role in the accumulation of evidence for perceptual decisions. These results are likely to add importance to the literature regarding the neural correlates of decision-making.

Strengths:

The use of TMS strengthens the evidence for the left SFS playing a causal role in the evidence accumulation process. By combining TMS with fMRI and advanced computational modelling of behaviour, the authors go beyond previous correlational studies in the field and provide converging behavioural, computational, and neural evidence of the specific role that the left SFS may play.

Sophisticated and rigorous analysis approaches are used throughout.

Weaknesses:

(3.1) Though the stimuli and motor responses were equalised between the perception and value-based decision tasks, reaction times (according to Figure 1) and potential difficulty (Figure 2) were not matched. Hence, differences in task difficulty might represent an alternative explanation for the effects being specific to the perception task rather than domain-specificity per se.

We agree that RTs cannot be matched a priori, and we did not intend them to be. Instead, we equated the inputs to the decision process and verified that each task relied exclusively on its task-relevant evidence. As reported in Results—Behaviour: validity of task-relevant pre-requisites (Fig. 1b–c), accuracy and RTs vary monotonically with the appropriate evidence regressor (SD for PDM; VD for VDM), with no effect of the task-irrelevant regressor. This separability check addresses differences in baseline RTs by showing that, for both tasks, behaviour tracks evidence as designed.

To rule out a generic difficulty account of the TMS effect, we relied on the within-subject differences-in-differences (DID) framework described in Methods (Differences-in-differences). The key Task × TMS interaction compares the pre→post change in PDM with the pre→post change in VDM while controlling for trialwise evidence and RT covariates. Any time-on-task or unspecific difficulty drift shared by both tasks is subtracted out by this contrast. Using this specification, TMS selectively reduced accuracy for PDM but not VDM (Fig. 3a; Supplementary Fig. 2a,c; Supplementary Tables 5–7).

Finally, the hierarchical DDM (already in the paper) dissociates latent mechanisms. The post-TMS boundary reduction appears only in PDM, whereas VDM shows a change in non-decision time without a decision-relevant parameter change (Fig. 3c; Supplementary Figs. 4–5). If unmatched difficulty were the sole driver, we would expect parallel effects across tasks, which we do not observe.

(3.2) No within- or between-participants sham/control TMS condition was employed. This would have strengthened the inference that the apparent TMS effects on behavioural and neural measures can truly be attributed to the left SFS stimulation and not to non-specific peripheral stimulation and/or time-on-task effects.

We agree that a sham/control condition would further strengthen causal attribution and note this as a limitation. In mitigation, our design incorporates several safeguards already reported in the manuscript:

· Within-subject pre/post with alternating task blocks and DID modelling (Methods) to difference out non-specific time-on-task effects.

· Task specificity across levels of analysis: behaviour (PDM accuracy reduction only), computational (boundary reduction only in PDM; no drift change), BOLD (reduced left-SFS accumulated-evidence signal for PDM but not VDM; Fig. 4a–c), and functional coupling (SFS–occipital PPI increase during PDM only; Fig. 5).

· Matched stimuli and motor outputs across tasks, so any peripheral sensations or general arousal effects should have influenced both tasks similarly; they did not.

Together, these converging task-selective effects reduce the likelihood that the results reflect non-specific stimulation or time-on-task. We will add an explicit statement in the Limitations noting the absence of sham/control and outlining it as a priority for future work.

(3.3) No a priori power analysis is presented.

We appreciate this point. Our sample size (n = 20) matched prior causal TMS and combined TMS–fMRI studies using similar paradigms and analyses (e.g., Philiastides et al., 2011; Rahnev et al., 2016; Jackson et al., 2021; van der Plas et al., 2021; Murd et al., 2021), and was chosen a priori on that basis and the practical constraints of cTBS + fMRI. The within-subject DID approach and hierarchical modelling further improve efficiency by leveraging all trials.

To address the reviewer’s request for transparency, we will (i) state this rationale in Methods—Participants, and (ii) ensure that all primary effects are reported with 95% CIs or posterior probabilities (already provided for the HDDM as pmcmcp_{\mathrm{mcmc}}pmcmc). We also note that the design was sensitive enough to detect RT changes in both tasks and a selective accuracy change in PDM, arguing against a blanket lack of power as an explanation for null VDM accuracy effects. We will nevertheless flag the absence of a formal prospective power analysis in the Limitations.

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

Some important elements of the methods are missing. How was the site for targeting the SFS with TMS identified? The methods described how M1 was located but not SFS.

Thank you for catching this omission. In the revised Methods we explicitly describe how the left SFS target was localized. Briefly, we used each participant’s T1-weighted anatomical scan and frameless neuronavigation to place a 10-mm sphere at the a priori MNI coordinates (x = −24, y = 24, z = 36) derived from prior work (Heekeren et al., 2004; Philiastides et al., 2011). This sphere was transformed to native space for each participant. The coil was positioned tangentially with the handle pointing posterior-lateral, and coil placement was continuously monitored with neuronavigation throughout stimulation. (All of these procedures mirror what we already report for M1 and are now stated for SFS as well.)

Where to revise the manuscript:

Methods → Stimulation protocol. After the first sentence naming cTBS, insert:<br /> “The left SFS target was localized on each participant’s T1-weighted anatomical image using frameless neuronavigation. A 10-mm radius sphere was centered at the a priori MNI coordinates x = −24, y = 24, z = 36 (Heekeren et al., 2004; Philiastides et al., 2011), then transformed to native space. The MR-compatible figure-of-eight coil was positioned tangentially over the target with the handle oriented posterior-laterally, and its position was tracked and maintained with neuronavigation during stimulation.”

It is not clear how participants were instructed that they should perform the value-difference task. Were they told that they should choose based on their original item value ratings or was it left up to them?

We agree the instruction should be explicit. Participants were told_: “In value-based blocks, choose the item you would prefer to eat at the end of the experiment.”_ They were informed that one VDM trial would be randomly selected for actual consumption, ensuring incentive-compatibility. We did not ask them to recall or follow their earlier ratings; those ratings were used only to construct evidence (value difference) and to define choice consistency offline.

Where to revise the manuscript:

Methods → Experimental paradigm.

Add a sentence to the VDM instruction paragraph:

“In value-based (LIKE) blocks, participants were instructed to choose the item they would prefer to consume at the end of the experiment; one VDM trial was randomly selected and implemented, making choices incentive-compatible. Prior ratings were used solely to construct value-difference evidence and to score choice consistency; participants were not asked to recall or match their earlier ratings.”

Line 86 Introduction, some previous studies were conducted on animals. Why it is problematic that the studies were conducted in animals is not stated. I assume the authors mean that we do not know if their findings will translate to the human brain? I think in fairness to those working with animals it might be worth an extra sentence to briefly expand on this point.

We appreciate this and will clarify that animal work is invaluable for circuit-level causality, but species differences and putative non-homologous areas (e.g., human SFS vs. rodent FOF) limit direct translation. Our point is not that animal studies are problematic, but that establishing causal roles in humans remains necessary.

Revision:

Introduction (paragraph discussing prior animal work). Replace the current sentence beginning “However, prior studies were largely correlational”

“Animal studies provide critical causal insights, yet direct translation to humans can be limited by species-specific anatomy and potential non-homologies (e.g., human SFS vs. frontal orienting fields in rodents). Therefore, establishing causal contributions in the human brain remains essential.”

Line 100-101: "or whether its involvement is peripheral and merely functionally supporting a larger system" - it is not clear what you mean by 'supporting a larger system'

We meant that observed SFS activity might reflect upstream/downstream support processes (e.g., attentional control or working-memory maintenance) rather than the computation of evidence accumulation itself. We have rephrased to avoid ambiguity.

Revision:

Introduction. Replace the phrase with:

“or whether its observed activity reflects upstream or downstream support processes (e.g., attention or working-memory maintenance) rather than the accumulation computation per se.”

The authors do have to make certain assumptions about the BOLD patterns that would be expected of an evidence accumulation region. These assumptions are reasonable and have been adopted in several previous neuroimaging studies. Nevertheless, it should be acknowledged that alternative possibilities exist and this is an inevitable limitation of using fMRI to study decision making. For example, if it turns out that participants collapse their boundaries as time elapses, then the assumption that trials with weaker evidence should have larger BOLD responses may not hold - the effect of more prolonged activity could be cancelled out by the lower boundaries. Again, I think this is just a limitation that could be acknowledged in the Discussion, my opinion is that this is the best effort yet to identify choice-relevant regions with fMRI and the authors deserve much credit for their rigorous approach.

Agreed. We already ground our BOLD regressors in the DDM literature, but acknowledge that alternative mechanisms (e.g., time-dependent boundaries) can alter expected BOLD–evidence relations. We now add a short limitation paragraph stating this explicitly.

Revision:

Discussion (limitations paragraph). Add:

“Our fMRI inferences rest on model-based assumptions linking accumulated evidence to BOLD amplitude. Alternative mechanisms—such as time-dependent (collapsing) boundaries—could attenuate the prediction that weaker-evidence trials yield longer accumulation and larger BOLD signals. While our behavioural and neural results converge under the DDM framework, we acknowledge this as a general limitation of model-based fMRI.”

Reviewer #2 (Recommendations For The Authors):

Minor points

I suggest the proportion of missed trials should be reported.

Thank you for the suggestion. In our preprocessing we excluded trials with no response within the task’s response window and any trials failing a priori validity checks. Because non-response trials contain neither a choice nor an RT, they are not entered into the DDM fits or the fMRI GLMs and, by design, carry no weight in the reported results. To keep the focus on the data that informed all analyses, we now (i) state the trial-inclusion criteria explicitly and (ii) report the number of analysed (valid) trials per task and run. This conveys the effective sample size contributing to each condition without altering the analysis set.

Revision:

Methods → (at the end of “Experimental paradigm”): “Analyses were conducted on valid trials only, defined as trials with a registered response within the task’s response window and passing pre-specified validity checks; trials without a response were excluded and not analysed.”

Results → “Behaviour: validity of task-relevant pre-requisites” (add one sentence at the end of the first paragraph): “All behavioural and fMRI analyses were performed on valid trials only (see Methods for inclusion criteria).”

Figure 4 c is very confusing. Is the legend or caption backwards?

Thanks for flagging. We corrected the Figure 4c caption to match the colouring and contrasts used in the panel (perceptual = blue/green overlays; value-based = orange/red; ‘post–pre’ contrasts explicitly labeled). No data or analyses were changed, just the wording to remove ambiguity.

Revision:

Figure 4 caption (panel c sentence). Replace with:

“(c) Post–pre contrasts for the trialwise accumulated-evidence regressor show reduced left-SFS BOLD during perceptual decisions (green overlay), with a significantly stronger reduction for perceptual vs value-based decisions (blue overlay). No reduction is observed for value-based decisions.”

Even if not statistically significant it may be of interest to add the results for Value-based decision making on SFS in Supplementary Table 3.

Done. We now include the SFS small-volume results for VDM (trialwise accumulated-evidence regressor) alongside the PDM values in the same table, with exact peak, cluster size, and statistics.

Revision:

Supplementary Table 3 (title):

“Regions encoding trialwise accumulated evidence (parametric modulation) during perceptual and value-based decisions, including SFS SVC results for both tasks.”

Model comparisons: please explain how model complexity is accounted for.

We clarify that model evidence was compared using the Deviance Information Criterion (DIC), which penalizes model fit by an effective number of parameters (pD). Lower DIC indicates better out-of-sample predictive performance after accounting for model complexity.

Revision:

Methods → Hierarchical Bayesian neural-DDM (last paragraph). Add:

“Model comparison used the Deviance Information Criterion (DIC = D̄ + pD), where pD is the effective number of parameters; thus DIC penalizes model complexity. Lower DIC denotes better predictive accuracy after accounting for complexity.”

Reviewer #3 (Recommendations For The Authors):

The following issues would benefit from clarification in the manuscript:

- It is stated that "Our sample size is well within acceptable range, similar to that of previous TMS studies." The sample size being similar to previous studies does not mean it is within an acceptable range. Whether the sample size is acceptable or not depends on the expected effect size. It is perfectly possible that the previous studies cited were all underpowered. What implications might the lack of an a priori power analysis have for the interpretation of the results?

We agree and have revised our wording. We did not conduct an a priori power analysis. Instead, we relied on a within-participant design that typically yields higher sensitivity in TMS–fMRI settings and on convergence across behavioural, computational, and neural measures. We now acknowledge that the absence of formal power calculations limits claims about small effects (particularly for null findings in VDM), and we frame those null results cautiously.

Revision:

Discussion (limitations). Add:

“The within-participant design enhances statistical sensitivity, yet the absence of an a priori power analysis constrains our ability to rule out small effects, particularly for null results in VDM.”

- I was confused when trying to match the results described in the 'Behaviour: validity of task-relevant pre-requisites' section on page 6 to what is presented in Figure 1. Specifically, Figure 1C is cited 4 times but I believe two of these should be citing Figure 1B?

Thank you—this was a citation mix-up. The two places that referenced “Fig. 1C” but described accuracy should in fact point to Fig. 1B. We corrected both citations.

Revision:

Results → Behaviour: validity… Change the two incorrect “Fig. 1C” references (when describing accuracy) to “Fig. 1B”.

- Also, where is the 'SD' coefficient of -0.254 (p-value = 0.123) coming from in line 211? I can't match this to the figure.

This was a typographical error in an earlier draft. The correct coefficients are those shown in the figure and reported elsewhere in the text (evidence-specific effects: for PDM RTs, SD β = −0.057, p < 0.001; for VDM RTs, VD β = −0.016, p = 0.011; non-relevant evidence terms are n.s.). We removed the erroneous value.

Revision:

Results → Behaviour: validity… (sentence with −0.254). Delete the incorrect value and retain the evidence-specific coefficients consistent with Fig. 1B–C.

- It is reported that reaction times were significantly faster for the perceptual relative to the value-based decision task. Was overall accuracy also significantly different between the two tasks? It appears from Figure 3 that it might be, But I couldn't find this reported in the text.

To avoid conflating task with evidence composition, we did not emphasize between-task accuracy averages. Our primary tests examine evidence-specific effects and TMS-induced changes within task. For completeness, we now report descriptive mean accuracies by task and point readers to the figure panels that display accuracy as a function of evidence (which is the meaningful comparison in our matched-evidence design). We refrain from additional hypothesis testing here to keep the analyses aligned with our preregistered focus.

Revision:

Results → Behaviour: validity… Add:

“For completeness, group-mean accuracies by task are provided descriptively in Fig. 3a; inferential tests in the manuscript focus on evidence-specific effects and TMS-induced changes within task.”

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

The manuscript by Yin and colleagues addresses a long-standing question in the field of cortical morphogenesis, regarding factors that determine differential cortical folding across species and individuals with cortical malformations. The authors present work based on a computational model of cortical folding evaluated alongside a physical model that makes use of gel swelling to investigate the role of a two-layer model for cortical morphogenesis. The study assesses these models against empirically derived cortical surfaces based on MRI data from ferret, macaque monkey, and human brains.

The manuscript is clearly written and presented, and the experimental work (physical gel modeling as well as numerical simulations) and analyses (subsequent morphometric evaluations) are conducted at the highest methodological standards. It constitutes an exemplary use of interdisciplinary approaches for addressing the question of cortical morphogenesis by bringing together well-tuned computational modeling with physical gel models. In addition, the comparative approaches used in this paper establish a foundation for broad-ranging future lines of work that investigate the impact of perturbations or abnormalities during cortical development.

The cross-species approach taken in this study is a major strength of the work. However, correspondence across the two methodologies did not appear to be equally consistent in predicting brain folding across all three species. The results presented in Figures 4 (and Figures S3 and S4) show broad correspondence in shape index and major sulci landmarks across all three species. Nevertheless, the results presented for the human brain lack the same degree of clear correspondence for the gel model results as observed in the macaque and ferret. While this study clearly establishes a strong foundation for comparative cortical anatomy across species and the impact of perturbations on individual morphogenesis, further work that fine-tunes physical modeling of complex morphologies, such as that of the human cortex, may help to further understand the factors that determine cortical functionalization and pathologies.

We thank the reviewer for positive opinions and helpful comments. Yes, the physical gel model of the human brain has a lower similarity index with the real brain. There are several reasons.

First, the highly convoluted human cortex has a few major folds (primary sulci) and a very large number of minor folds associated with secondary or tertiary sulci (on scales of order comparable to the cortical thickness), relative to the ferret and macaque cerebral cortex. In our gel model, the exact shapes, positions, and orientations of these minor folds are stochastic, which makes it hard to have a very high similarity index of the gel models when compared with the brain of a single individual.

Second, in real human brains, these minor folds evolve dynamically with age and show differences among individuals. In experiments with the gel brain, multiscale folds form and eventually disappear as the swelling progresses through the thickness. Our physical model results are snapshots during this dynamical process, which makes it hard to have a concrete one-to-one correspondence between the instantaneous shapes of the swelling gel and the growing human brain.

Third, the growth of the brain cortex is inhomogeneous in space and varying with time, whereas, in the gel model, swelling is relatively homogeneous.

We agree that further systematic work, based on our proposed methods, with more fine-tuned gel geometries and properties, might provide a deeper understanding of the relations between brain geometry, and growth-induced folds and their functionalization and pathologies. Further analysis of cortical pathologies using computational and physical gel models can be found in our companion paper (Choi et al., 2025), also published in eLife:

G. P. T. Choi, C. Liu, S. Yin, G. Séjourné, R. S. Smith, C. A. Walsh, L. Mahadevan, Biophysical basis for brain folding and misfolding patterns in ferrets and humans. eLife, 14, RP107141, 2025. doi:10.7554/eLife.107141

Reviewer# 2 (Public review):

This manuscript explores the mechanisms underlying cerebral cortical folding using a combination of physical modelling, computational simulations, and geometric morphometrics. The authors extend their prior work on human brain development (Tallinen et al., 2014; 2016) to a comparative framework involving three mammalian species: ferrets (Carnivora), macaques (Old World monkeys), and humans (Hominoidea). By integrating swelling gel experiments with mathematical differential growth models, they simulate sulcification instability and recapitulate key features of brain folding across species. The authors make commendable use of publicly available datasets to construct 3D models of fetal and neonatal brain surfaces: fetal macaque (ref. [26]), newborn ferret (ref. [11]), and fetal human (ref. [22]).

Using a combination of physical models and numerical simulations, the authors compare the resulting folding morphologies to real brain surfaces using morphometric analysis. Their results show qualitative and quantitative concordance with observed cortical folding patterns, supporting the view that differential tangential growth of the cortex relative to the subcortical substrate is sufficient to account for much of the diversity in cortical folding. This is a very important point in our field, and can be used in the teaching of medical students.

Brain folding remains a topic of ongoing debate. While some regard it as a critical specialization linked to higher cognitive function, others consider it an epiphenomenon of expansion and constrained geometry. This divergence was evident in discussions during the Strungmann Forum on cortical development (Silver¨ et al., 2019). Though folding abnormalities are reliable indicators of disrupted neurodevelopmental processes (e.g., neurogenesis, migration), their relationship to functional architecture remains unclear. Recent evidence suggests that the absolute number of neurons varies significantly with position-sulcus versus gyrus-with potential implications for local processing capacity (e.g., https://doi.org/10.1002/cne.25626). The field is thus in need of comparative, mechanistic studies like the present one.

This paper offers an elegant and timely contribution by combining gel-based morphogenesis, numerical modelling, and morphometric analysis to examine cortical folding across species. The experimental design - constructing two-layer PDMS models from 3D MRI data and immersing them in organic solvents to induce differential swelling - is well-established in prior literature. The authors further complement this with a continuum mechanics model simulating folding as a result of differential growth, as well as a comparative analysis of surface morphologies derived from in vivo, in vitro, and in silico brains.

We thank the reviewer for the very positive comments.

I offer a few suggestions here for clarification and further exploration:

Major Comments

(1) Choice of Developmental Stages and Initial Conditions

The authors should provide a clearer justification for the specific developmental stages chosen (e.g., G85 for macaque, GW23 for human). How sensitive are the resulting folding patterns to the initial surface geometry of the gel models? Given that folding is a nonlinear process, early geometric perturbations may propagate into divergent morphologies. Exploring this sensitivity-either through simulations or reference to prior work-would enhance the robustness of the findings.

The initial geometry is one of the important factors that decides the final folding pattern. The smooth brain in the early developmental stage shows a broad consistency across individuals, and we expect the main folds to form similarly across species and individuals.

Generally, we choose the initial geometry when the brain cortex is still relatively smooth. For the human, this corresponds approximately to GW23, as the major folds such as the Rolandic fissure (central sulcus), arise during this developmental stage. For the macaque brain, we chose developmental stage G85, primarily because of the availability of the dataset corresponding to this time, which also corresponds to the least folded.

We expect that large-scale folding patterns are strongly sensitive to the initial geometry but fine-scale features are not. Since our goal is to explain the large-scale features, we expect sensitivity to the initial shape.

Below are some references of other researchers that are consistent with this idea. Figure 4 from Wang et al. shows some images of simulations obtained by perturbing the geometry of a sphere to an ellipsoid. We see that the growth-induced folds mostly maintain their width (wavelength), but change their orientations.

Reference:

Wang, X., Lefévre, J., Bohi, A., Harrach, M.A., Dinomais, M. and Rousseau, F., 2021. The influence of biophysical parameters in a biomechanical model of cortical folding patterns. Scientific Reports, 11(1), p.7686.

Related results from the same group show that slight perturbations of brain geometry, cause these folds also tend to change their orientations but not width/wavelength (Bohi et al., 2019).

Reference:

Bohi, A., Wang, X., Harrach, M., Dinomais, M., Rousseau, F. and Lefévre, J., 2019, July. Global perturbation of initial geometry in a biomechanical model of cortical morphogenesis. In 2019 41st Annual International Conference of the IEEE Engineering in Medicine and Biology Society (EMBC) (pp. 442-445). IEEE.

Finally, a systematic discussion of the role of perturbations on the initial geometries and physical properties can be seen in our work on understanding a different system, gut morphogenesis (Gill et al., 2024).

We have added the discussion about geometric sensitivity in the section Methods-Numerical Simulations:

“Small perturbations on initial geometry would affect minor folds, but the main features of major folds, such as orientations, width, and depth, are expected to be conserved across individuals [49, 50]. For simplicity, we do not perturb the fetal brain geometry obtained from datasets.”

(2) Parameter Space and Breakdown Points

The numerical model assumes homogeneous growth profiles and simplifies several aspects of cortical mechanics. Parameters such as cortical thickness, modulus ratios, and growth ratios are described in Table II. It would be informative to discuss the range of parameter values for which the model remains valid, and under what conditions the physical and computational models diverge. This would help delineate the boundaries of the current modelling framework and indicate directions for refinement.

Exploring the valid parameter space is a key problem. We have tested a series of growth parameters and will state them explicitly in our revision. In the current version, we chose the ones that yield a relatively high similarity index to the animal brains. More generally, folding patterns are largely regulated by geometry as well as physical parameters, such as cortical thickness, modulus ratios, growth ratios, and inhomogeneity. In our previous work on a different system, gut morphogenesis, where similar folding patterns are seen, we have explored these features (Gill et al., 2024).

Reference:

Gill, H.K., Yin, S., Nerurkar, N.L., Lawlor, J.C., Lee, C., Huycke, T.R., Mahadevan, L. and Tabin, C.J., 2024. Hox gene activity directs physical forces to differentially shape chick small and large intestinal epithelia. Developmental Cell, 59(21), pp.2834-2849.

(3) Neglected Regional Features: The Occipital Pole of the Macaque

One conspicuous omission is the lack of attention to the occipital pole of the macaque, which is known to remain smooth even at later gestational stages and has an unusually high neuronal density (2.5× higher than adjacent cortex). This feature is not reproduced in the gel or numerical models, nor is it discussed. Acknowledging this discrepancy-and speculating on possible developmental or mechanical explanationswould add depth to the comparative analysis. The authors may wish to include this as a limitation or a target for future work.

Yes, we have added that the omission of the Occipital Pole of the macaque is one of our paper’s limitations. Our main aim in this paper is to explore the formation of large-scale folds, so the smooth region is not discussed. But future work could include this to make the model more complete.

The main text has been modified in Methods, Numerical simulations:

“To focus on fold formation, we did not discuss the relatively smooth region, such as the Occipital Pole of the macaque.”

and also in the caption of Figure 4: “... The occipital pole region of macaque brains remains smooth in real and simulated brains.”

(4) Spatio-Temporal Growth Rates and Available Human Data

The authors note that accurate, species-specific spatio-temporal growth data are lacking, limiting the ability to model inhomogeneous cortical expansion. While this may be true for ferret and macaque, there are high-quality datasets available for human fetal development, now extended through ultrasound imaging (e.g., https://doi.org/10.1038/s41586-023-06630-3). Incorporating or at least referencing such data could improve the fidelity of the human model and expand the applicability of the approach to clinical or pathological scenarios.

We thank the reviewer for pointing out the very useful datasets that exist for the exploration of inhomogeneous growth driven folding patterns. We have referred to this paper to provide suggestions for further work in exploring the role of growth inhomogeneities.

We have referred to this high-quality dataset in our main text, Discussion:

“...the effect of inhomogeneous growth needs to be further investigated by incorporating regional growth of the gray and white matter not only in human brains [29, 31] based on public datasets [45], but also in other species.”

A few works have tried to incorporate inhomogeneous growth in simulating human brain folding by separating the central sulcus area into several lobes (e.g., lobe parcellation method, Wang, PhD Thesis, 2021). Since our goal in this paper is to explain the large-scale features of folding in a minimal setting, we have kept our model simple and show that it is still capable of capturing the main features of folding in a range of mammalian brains.

Reference:

Xiaoyu Wang. Modélisation et caractérisation du plissement cortical. Signal and Image Processing. Ecole nationale superieure Mines-Télécom Atlantique, 2021. English. 〈NNT : 2021IMTA0248〉.

(5) Future Applications: The Inverse Problem and Fossil Brains

The authors suggest that their morphometric framework could be extended to solve the inverse growth problem-reconstructing fetal geometries from adult brains. This speculative but intriguing direction has implications for evolutionary neuroscience, particularly the interpretation of fossil endocasts. Although beyond the scope of this paper, I encourage the authors to elaborate briefly on how such a framework might be practically implemented and validated.

For the inverse problem, we could use the following strategies:

a. Perform systematic simulations using different geometries and physical parameters to obtain the variation in morphologies as a function of parameters.

b. Using either supervised training or unsupervised training (physics-informed neural networks, PINNs) to learn these characteristic morphologies and classify their dependence on the parameters using neural networks. These can then be trained to determine the possible range of geometrical and physical parameters that yield buckled patterns seen in the systematic simulations.

c. Reconstruct the 3D surface from fossil endocasts. Using the well-trained neural network, it should be possible to predict the initial shape of the smooth brain cortex, growth profile, and stiffness ratio of the gray and white matter.

As an example in this direction, supervised neural networks have been used recently to solve the forward problem to predict the buckling pattern of a growing two-layer system (Chavoshnejad et al., 2023). The inverse problem can then be solved using machine-learning methods when the training datasets are the folded shape, which are then used to predict the initial geometry and physical properties.

Reference:

Chavoshnejad, P., Chen, L., Yu, X., Hou, J., Filla, N., Zhu, D., Liu, T., Li, G., Razavi, M.J. and Wang, X., 2023. An integrated finite element method and machine learning algorithm for brain morphology prediction. Cerebral Cortex, 33(15), pp.9354-9366.

Conclusion

This is a well-executed and creative study that integrates diverse methodologies to address a longstanding question in developmental neurobiology. While a few aspects-such as regional folding peculiarities, sensitivity to initial conditions, and available human data-could be further elaborated, they do not detract from the overall quality and novelty of the work. I enthusiastically support this paper and believe that it will be of broad interest to the neuroscience, biomechanics, and developmental biology communities.

Note: The paper mentions a companion paper [reference 11] that explores the cellular and anatomical changes in the ferret cortex. I did not have access to this manuscript, but judging from the title, this paper might further strengthen the conclusions.

The companion paper (Choi et al., 2025) has also been submitted to eLife and can be found here:

G. P. T. Choi, C. Liu, S. Yin, G. Séjourné, R. S. Smith, C. A. Walsh, L. Mahadevan, Biophysical basis for brain folding and misfolding patterns in ferrets and humans. eLife, 14, RP107141, 2025. doi:10.7554/eLife.107141

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

This study was conducted and presented to the highest methodological standards. It is clearly written, and the results are thoroughly presented in the main manuscript and supplementary materials. Nevertheless, I would present the following minor points and comments for consideration by the authors prior to finalizing their work:

We thank the reviewer for positive opinions and helpful comments.

(1) Where did the MRI-based cortical surface data come from? Specifically, it would be helpful to include more information regarding whether the surfaces were reconstructed based on individual- or group-level data. It appears the surfaces were group-level, and, if so, accounting for individual-level cortical folding may be a fruitful direction for future work.

The surface data come from public database, which are stated in the Methods Section. “We used a publicly available database for all our 3d reconstructions: fetal macaque brain surfaces are obtained from Liu et al. (2020); newborn ferret brain surfaces are obtained from Choi et al. (2025); and fetal human brain surfaces are obtained from Tallinen et al. (2016).”

These surfaces are reconstructed based on group-level data. Specifically, the macaque atlas images are constructed for brains at gestational ages of 85 days (G85, N \=18_, 9 females), 110 days (G110, _N \=10_, 7 females) and 135 days (G135, _N \=16_,_ 7 females). And yes, future work may focus on individual-level cortical folding, and we expect that more specific results could be found.

(2) One methodological approach for assessing consistency of cortical folding within species might be an evaluation of cross-hemispheric symmetry. I would find this particularly interesting with respect to the gel models, as it could complement the quantification of variation with respect to the computationally derived and real surfaces.

Yes, the cross-hemispheric symmetry comparison can be done by our morphometric analysis method. We have added the results of ferret brain’s left-right symmetry for gel models, simulations, and real surfaces in the supplementary material. A typical conformal mapping figure and the similarity index table are shown here.

(3) Was there a specific reason to reorder the histogram plots in Figure 4c to macaque, ferret, human rather than to maintain the order presented in Figure 4a/b of ferret, macaque, human? I appreciate that this is a minor concern, and all subplots are indeed properly titled, but consistent order may improve clarity.

We have reordered the histogram plots to make all the figure orders consistent.

Reviewer #2 (Recommendations for the authors):

(1) Please consider revising the caption of Figure 1 (or equivalent figures) to explicitly state whether features such as the macaque occipital flatness were reproduced or not.

We thank the reviewer for pointing out the macaque occipital flatness.

Author response table 1.

Left-right similarity index evaluated by comparing the shape index of ferret brains, calculated with vector P-NORM p\=2,

Author response image 1.

Left-right similarity index of ferret brains

Occipital Pole of the macaque remains relatively smooth in both real brains and computational models. But our main aim in this paper is to explore the large-scale folds formation, so the smooth region is not discussed in depth. But future work could include this to make the model more complete.

(2) Some figures could benefit from clearer labelling to distinguish between in vivo, in vitro, and in silico results.

We have supplemented some texts in panels to make the labelling clearer.

(3) The manuscript would benefit from a short paragraph in the Discussion reflecting on how future incorporation of regional heterogeneities might improve model fidelity.

We have added a sentence in the Discussion Section about improving the model fidelity by considering regional heterogeneities.

“Future more accurate models incorporating spatio-temporal inhomogeneous growth profiles and mechanical properties, such as varying stiffness, would make the folding pattern closer to the real cortical folding. This relies on more in vivo measurements of the brain’s physical properties and cortical expansion.”

(4) Suggestions for improved or additional experiments, data, or analyses.

(5) Clarify and justify the selection of developmental stages: The authors should explain why particular gestational stages (e.g., G85 for macaque, GW23 for human) were chosen as starting points for the physical and computational models. A discussion of how sensitive the folding patterns are to the initial geometry would help assess the robustness of the model. If feasible, a brief sensitivity analysis-varying initial age or surface geometry-would strengthen the conclusions.

The initial geometry is one of the important factors that decides the final folding pattern. The smooth brain in the early developmental stage shows a broad consistency across individuals, and we expect the main folds to form similarly across species and individuals.

Generally, we choose the initial geometry when the brain cortex is still relatively smooth. For the human, this corresponds approximately to GW23, as the major folds such as the Rolandic fissure (central sulcus), arise during this developmental stage. For the macaque brain, we chose developmental stage G85, primarily because of the availability of the dataset corresponding to this time, which also corresponds to the least folded.

We expect that large-scale folding patterns are strongly sensitive to the initial geometry but fine-scale features are not. Since our goal is to explain the large-scale features, we expect sensitivity to the initial shape.

We have added the discussion about geometric sensitivity in the section Methods-Numerical Simulations: “Small perturbations on initial geometry would affect minor folds, but the main features of major folds, such as orientations, width, and depth, are expected to be conserved across individuals [49, 50]. For simplicity, we do not perturb the fetal brain geometry obtained from datasets.”

(6) Explore parameter boundaries more explicitly: The paper would benefit from a clearer account of the ranges of mechanical and geometric parameters (e.g., growth ratios, cortical thickness) for which the model holds. Are there specific conditions under which the physical and numerical models diverge? Identifying breakdown points would help readers understand the model’s limitations and applicability.

Exploring the valid parameter space is a key problem. We have tested a series of growth parameters and will state them explicitly in our revision. In the current version, we chose the ones that yield a relatively high similarity index to the animal brains. More generally, folding patterns are largely regulated by geometry as well as physical parameters, such as cortical thickness, modulus ratios, and growth ratios and inhomogeneity. In our previous work on a different system, gut morphogenesis, where similar folding patterns are seen, we have explored these features (Gill et al., 2024).

(7) Address species-specific cortical peculiarities: A striking omission is the flat occipital pole of the macaque, which is not reproduced in the physical or computational models. Given its known anatomical and cellular distinctiveness, this discrepancy warrants discussion. Even if not explored experimentally, the authors could speculate on what developmental or mechanical conditions would be needed to reproduce such regional smoothness.

Please refer to our answer to the public reviewer 2, question (3). From our results, the formation of smooth Occipital Pole might indicate that the spatio-temporal growth rate of gray and white matter are consistent in this region, such that there’s no much differential growth.

(8) Consider integration of available human growth data: While the authors note the lack of spatiotemporal growth data across species, such datasets exist for human fetal brain development, including those from MRI and ultrasound studies (e.g., Nature 2023). Incorporating these into the human model-or at least discussing their implications-would enhance biological relevance.

Yes, some datasets for fetal human brains have provided very comprehensive measurements on brain shapes at many developmental stages. This can surely be implemented in our current model by calculating the spatio-temporal growth rate from regional cortical shapes at different stages.

(9) Recommendations for improving the writing and presentation:

a) The manuscript is generally well-written, but certain sections would benefit from more explicit linksbetween the biological phenomena and the modeling framework. For instance, the Introduction and Discussion could more clearly articulate how mechanical principles interface with genetic or cellular processes, especially in the context of evolution and developmental variation.

We have briefly discussed the gene-regulated cellular process and the induced changes of mechanical properties and growth rules in SI, table S1. In the main text, to be clearer, we have added a sentence:

“Many malformations are related to gene-regulated abnormal cellular processes and mechanical properties, which are discussed in SI”

b) The Discussion could better acknowledge limitations and future directions, including regional dif-ferences in folding, inter-individual variability, and the model’s assumptions of homogeneous material properties and growth.

In the discussion section, we have pointed out four main limitations and open directions based on our current model, including the discussion on spatiotemporal growth and property. To be more complete, we have supplemented other limitations on the regional differences in folding and the interindividual variability. In the main text, we added the following sentence:

“In addition to the homogeneity assumption, we have not investigated the inter-individual variability and regional differences in folding. More accurate and specific work is expected to focus on these directions.”

c) The authors briefly mention the potential for addressing the inverse growth problem. Expanding this idea in a short paragraph - perhaps with hypothetical applications to fossil brain reconstructions-would broaden the paper’s appeal to evolutionary neuroscientists.

We have stated general steps in the response to public reviewer 2, question (5).

(10) Minor corrections to the text and figures:

a) Figures:

Label figures more clearly to distinguish between in vivo, in vitro, and in silico brain representations.– Ensure that the occipital pole of the macaque is visible or annotated, especially if it lacks the expected smoothness.

Add scale bars where missing for clarity in morphometric comparisons.

We thank the reviewer for suggestions to improve the readability of our manuscript.

The in vivo (real), in vitro (gel), and in silico (simulated) results are both distinguished by their labels and different color scheme: gray-white for real brain, pink-white for gel model, and blue-white for simulations, respectively.

The occipital pole of the macaque brain remains relatively smooth in our computational model but notin our physical gel model. We have clarified this in the main text: “To focus on fold formation, we did not discuss the relatively smooth region, such as the Occipital Pole of the macaque.”

All the brain models are rescaled to the same size, where the distance between the anterior-most pointof the frontal lobe and the posterior-most point of the occipital lobe is two units.

b) Text:

Consider revising figure captions to explicitly mention whether specific regional features (e.g., flatoccipital pole) were observed or absent in models.

In Table II (and relevant text), ensure parameter definitions are consistent and explained clearly for across-disciplinary audience.

Add citations to recent human fetal growth imaging work (e.g., ultrasound-based studies) to support claims about available data.

We have added some descriptions of the characters of the folding pattern in the caption of Figure 4,including major folds and smooth regions.

“Three or four major folds of each brain model are highlighted and served as landmarks. The occipital pole region of macaque brains remains smooth in real and simulated brains.”

We have clarified the definition of growth ratio gMsub>g</sub>/g_w and stiffness ratio µ_g/µ_w between gray matter and white matter, and the normalized cortical thickness h/L in Table 2.

We have referred to a high-quality dataset of fetal brain imaging work, the ultrasound-imaging method(Namburete et al. 2023), in our main text, Discussion:

“...the effect of inhomogeneous growth needs to be further investigated by incorporating regional growth of the gray and white matter not only in human brains [29, 31] based on public datasets [45], but also in other species.”

Author response:

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

Reviewer #1 (Public review):

Lack of Sensitivity Analyses for some Key Methodological Decisions: Certain methodological choices in this manuscript diverge from approaches used in previous works. In these cases, I recommend the following: (i) The authors could provide a clear and detailed justification for these deviations from established methods, and (ii) supplementary sensitivity analyses could be included to ensure the robustness of the findings, demonstrating that the results are not driven primarily by these methodological changes. Below, I outline the main areas where such evaluations are needed:

This detailed guidance is incredibly valuable, and we are grateful. Work of this kind is in its relative infancy, and there are so many design choices depending on the data available, questions being addressed, and so on. Help us navigate that has been extremely useful. In our revised manuscript we are very happy to add additional justification for design choices made, and wherever possible test the impact of those choices. It is certainly the case that different approaches have been used across the handful of papers published in this space, and, unlike in other areas of systems neuroscience, we have yet to reach the point where any of these approaches are established. We agree with the reviewer that wherever possible these design choices should be tested. 

Use of Communicability Matrices for Structural Connectivity Gradients: The authors chose to construct structural connectivity gradients using communicability matrices, arguing that diffusion map embedding "requires a smooth, fully connected matrix." However, by definition, the creation of the affinity matrix already involves smoothing and ensures full connectedness. I recommend that the authors include an analysis of what happens when the communicability matrix step is omitted. This sensitivity test is crucial, as it would help determine whether the main findings hold under a simpler construction of the affinity matrix. If the results significantly change, it could indicate that the observations are sensitive to this design choice, thereby raising concerns about the robustness of the conclusions. Additionally, if the concern is related to the large range of weights in the raw structural connectivity (SC) matrix, a more conventional approach is to apply a log-transformation to the SC weights (e.g., log(1+𝑆𝐶_𝑖𝑗)), which may yield a more reliable affinity matrix without the need for communicability measures.

The reason we used communicability is indeed partly because we wanted to guarantee a smooth fully connected matrix, but also because our end goal for this project was to explore structure-function coupling in these low-dimensional manifolds.  Structural communicability – like standard metrics of functional connectivity – includes both direct and indirect pathways, whereas streamline counts only capture direct communication. In essence we wanted to capture not only how information might be routed from one location to another, but also the more likely situation in which information propagates through the system. 

In the revised manuscript we have given a clearer justification for why we wanted to use communicability as our structural measure (Page 4, Line 179):

“To capture both direct and indirect paths of connectivity and communication, we generated weighted communicability matrices using SIFT2-weighted fibre bundle capacity (FBC). These communicability matrices reflect a graph theory measure of information transfer previously shown to maximally predict functional connectivity (Esfahlani et al., 2022; Seguin et al., 2022). This also foreshadowed our structure-function coupling analyses, whereby network communication models have been shown to increase coupling strength relative to streamline counts (Seguin et al., 2020)”.

We have also referred the reader to a new section of the Results that includes the structural gradients based on the streamline counts (Page 7, line 316):

“Finally, as a sensitivity analysis, to determine the effect of communicability on the gradients, we derived affinity matrices for both datasets using a simpler measure: the log of raw streamline counts. The first 3 components derived from streamline counts compared to communicability were highly consistent across both NKI  (r_s = 0.791, r_s = 0.866, r_s = 0.761) and the referred subset of CALM (r_s = 0.951, r_s = 0.809, r_s = 0.861), suggesting that in practice the organisational gradients are highly similar regardless of the SC metric used to construct the affinity matrices”. 

Methodological ambiguity/lack of clarity in the description of certain evaluation steps: Some aspects of the manuscript’s methodological description are ambiguous, making it challenging for future readers to fully reproduce the analyses based on the information provided. I believe the following sections would benefit from additional detail and clarification:

Computation of Manifold Eccentricity: The description of how eccentricity was computed (both in the results and methods sections) is unclear and may be problematic. The main ambiguity lies in how the group manifold origin was defined or computed. (1) In the results section, it appears that separate manifold origins were calculated for the NKI and CALM groups, suggesting a dataset-specific approach. (2) Conversely, the methods section implies that a single manifold origin was obtained by somehow combining the group origins across the three datasets, which seems contradictory. Moreover, including neurodivergent individuals in defining the central group manifold origin in conceptually problematic. Given that neurodivergent participants might exhibit atypical brain organization, as suggested by Figure 1, this inclusion could skew the definition of what should represent a typical or normative brain manifold. A more appropriate approach might involve constructing the group manifold origin using only the neurotypical participants from both the NKI and CALM datasets. Given the reported similarity between group-level manifolds of neurotypical individuals in CALM and NKI, it would be reasonable to expect that this combined origin should be close to the origin computed within neurotypical samples of either NKI or CALM. As a sanity check, I recommend reporting the distance of the combined neurotypical manifold origin to the centres of the neurotypical manifolds in each dataset. Moreover, if the manifold origin was constructed while utilizing all samples (including neurodivergent samples) I think this needs to be reconsidered. 

This is a great point, and we are very happy to clarify. Separate manifolds were calculated for the NKI and CALM participants, hence a dataset-specific approach. Indeed, in the long-run our goal was to explore individual differences in these manifolds, relative to the respective group-level origins, and their intersection across modalities, so manifold eccentricity was calculated at an individual level for subsequent analyses. At the group level, for each modality, we computed 3 manifold origins: one for NKI, one for the referred subset of CALM, and another for the neurotypical portion of CALM. Crucially, because the manifolds are always normal, in each case the manifold origin point is near-zero (extremely near-zero, to the 6^th or 7^th decimal place). In other words, we do indeed calculate the origin separately each time we calculate the gradients, but the origin is zero in every case. As a result, differences in the origin point cannot be the source of any differences we observe in manifold eccentricity between groups or individuals. We have updated the Methods section with the manifold origin points for each dataset and clarified our rationale (Page 16, Line 1296):

“Note that we used a dataset-specific approach when we computed manifold eccentricity for each of the three groups relative to their group-level origin: neurotypical CALM (SC origin = -7.698 x 10^-7, FC origin = 6.724 x 10^-7), neurodivergent CALM (SC origin = -6.422 x 10 , FC origin = 1.363 x 10 ), and NKI (SC origin = -7.434 x 10 , FC origin = 4.308 x 10^-6). Eccentricity is a relative measure and thus normalised relative to the origin. Because of this normalisation, each time gradients are constructed the manifold origin is necessarily near-zero, meaning that differences in manifold eccentricity of individual nodes, either between groups or individuals, are stem from the eccentricity of that node rather than a difference in origin point”. 

We clarified the computation of the respective manifold origins within the Results section, and referred the reader to the relevant Methods section (Page 9, line 446):

“For each modality (2 levels: SC and FC) and dataset (3 levels: neurotypical CALM, neurodivergent CALM, and NKI), we computed the group manifold origin as the mean of their respective first three gradients. Because of the normal nature of the manifolds this necessarily means that these origin points will be very near-zero, but we include the exact values in the ‘Manifold Eccentricity’ methodology sub-section”. 

Individual-Level Gradients vs. Group-Level Gradients: Unlike previous studies that examined alterations in principal gradients (e.g., Xia et al., 2022; Dong et al., 2021), this manuscript focuses on gradients derived directly from individual-level data. In contrast, earlier works have typically computed gradients based on grouped data, such as using a moving window of individuals based on age (Xia et al.) or evaluating two distinct age groups (Dong et al.). I believe it is essential to assess the sensitivity of the findings to this methodological choice. Such an evaluation could clarify whether the observed discrepancies with previous reports are due to true biological differences or simply a result of different analytical strategies.

This is a brilliant point. The central purpose of our project was to test how individual differences in these gradients, and their intersection across modalities, related to differences in phenotype (e.g. cognitive difficulties). These necessitated calculating gradients at the level of individuals and building a pipeline to do so, given that we could find no other examples. Nonetheless, despite this different goal and thus approach, we had expected to replicate a couple of other key findings, most prominently the ‘swapping’ of gradients shown by Dong et al. (2021). We were also surprised that we did not find this changing in order. The reviewer is right and there could be several design features that produce the difference, and in the revised manuscript we test several of them. We have added the following text to the manuscript as a sensitivity analysis for the Results sub-section titled “Stability of individual-level gradients across developmental time” (Page 7, Line 344 onwards):

“One possibility is that our observation of gradient stability – rather than a swapping of the order for the first two gradients (Dong et al., 2021) – is because we calculated them at an individual level. To test this, we created subgroups and contrasted the first two group-level structural and functional gradients derived from children (younger than 12 years old) versus those from adolescents (12 years old and above), using the same age groupings as prior work (Dong et al., 2021). If our use of individually calculated gradients produces the stability, then we should observe the swapping of gradients in this sensitivity analysis. Using baseline scans from NKI, the primary structural gradient in childhood (N = 99) as shown in Figure 1f, this was highly correlated (r_s = 0.995) with those derived from adolescents (N = 123). Likewise, the secondary structural gradient in childhood was highly consistent in adolescence (r_s = 0.988). In terms of functional connectivity, the principal gradient in childhood (N = 88) was highly consistent in adolescence (r_s = 0.990, N = 125). The secondary gradient in childhood was again highly similar in adolescence (r_s = 0.984). The same result occurred in the CALM dataset: In the baseline referred subset of CALM, the primary and secondary communicability gradients derived from children (N = 258) and adolescents (N = 53) were near-identical (r_s = 0.991 and r_s = 0.967, respectively). Alignment for the primary and secondary functional gradients derived from children (N = 130) and adolescents (N = 43) were also near-identical (r_s = 0.972 and r_s = 0.983, respectively). These consistencies across development suggest that gradients of communicability and functional connectivity established in childhood are the same as those in adolescence, irrespective of group-level or individual-level analysis. Put simply, our failure to replicate the swapping of gradient order in Dong et al. (2021) is not the result of calculating gradients at the level of individual participants.”

Procrustes Transformation: It is unclear why the authors opted to include a Procrustes transformation in this analysis, especially given that previous related studies (e.g., Dong et al.) did not apply this step. I believe it is crucial to evaluate whether this methodological choice influences the results, particularly in the context of developmental changes in organizational gradients. Specifically, the Procrustes transformation may maximize alignment to the group-level gradients, potentially masking individual-level differences. This could result in a reordering of the gradients (e.g., swapping the first and second gradients), which might obscure true developmental alterations. It would be informative to include an analysis showing the impact of performing vs. omitting the Procrustes transformation, as this could help clarify whether the observed effects are robust or an artifact of the alignment procedure. (Please also refer to my comment on adding a subplot to Figure 1). Additionally, clarifying how exactly the transformation was applied to align gradients across hemispheres, individuals, and/or datasets would help resolve ambiguity. 

The current study investigated individual differences in connectome organisation, rather than group-level trends (Dong et al., 2021). This necessitates aligning individual gradients to the corresponding group-level template using a Procrustes rotation. Without a rotation, there is no way of knowing if you are comparing  ‘like with like’: the manifold eccentricity of a given node may appear to change across individuals simply due to subtle differences in the arbitrary orientation of the underlying manifolds. We also note that prior work examining individual differences in principal alignment have used Procrustes (Xia et al., 2022), who demonstrated emergence of the principal gradient across development, albeit with much smaller effects than Dong and colleagues (2021). Nonetheless, we agree, the Procrustes rotation could be another source of the differences we observed with the previous paper (Dong et al. 2021). We explored the impact of the Procrustes rotation on individual gradients as our next sensitivity analysis. We recalculated everyone’s gradients without Procrustes rotation. We then tested the alignment of each participant with the group-level gradients using Spearman’s correlations, followed by a series of generalised linear models to predict principal gradient alignment using head motion, age, and sex. The expected swapping of the first and second functional gradient (Dong et al., 2021) would be represented by a decrease in the spatial similarity of each child’s principal functional gradient to the principal childhood group-level gradient, at the onset of adolescence (~age 12). However, there is no age effect on this unrotated alignment, suggesting that the lack of gradient swapping in our data does not appear to be the result of the Procrustes rotation. When you use unrotated individual gradients the alignment is remarkably consistent across childhood and adolescence. Alignment is, however, related to head motion, which is often related to age. To emphasise the importance of motion, particularly in relation to development, we conducted a mediation analysis between the relationship between age and principal alignment (without correcting for motion), with motion as a mediator, within the NKI dataset. Before accounting for motion, the relationship between age and principal alignment is significant, but this can be entirely accounted for by motion. In our revised manuscript we have included this additional analysis in the Results sub-section titled “Stability of individual-level gradients across developmental time”, following on from the above point about the effect of group-level versus individual-level analysis (Page 8, Line 400):

“A second possible discrepancy between our results and that of prior work examining developmental change in group-level functional gradients (Dong et al., 2021) was the use of Procrustes alignment. Such alignment of individual-level gradients to group-level templates is a necessary step to ensure valid comparisons between corresponding gradients across individuals, and has been implemented in sliding-window developmental work tracking functional gradient development (Xia et al., 2022). Nonetheless, we tested whether our observation of stable principal functional and communicability gradients may be an artefact of the Procrustes rotation. We did this by modelling how individual-level alignment without Procrustes rotation to the group-level templates varies with age, head motion, and sex, as a series of generalised linear models. We included head motion as the magnitude of the Procrustes rotation has been shown to be positively correlated with mean framewise displacement (Sasse et al., 2024), and prior group-level work (Dong et al., 2021) included an absolute motion threshold rather than continuous motion estimates. Using the baseline referred CALM sample, there was no significant relationship between alignment and age (β = -0.044, 95% CI = [-0.154, 0.066], p = 0.432) after accounting for head motion and sex. Interestingly, however head motion was significantly associated with alignment ( β = -0.318, 95% CI = [-0.428, -.207], p = 1.731 x 10^-8), such that greater head motion was linked to weaker alignment. Note that older children tended to have exhibit less motion for their structural scans (r_s = 0.335, p < 0.001). We observed similar trends in functional alignment, whereby tighter alignment was significantly predicted by lower head motion (β = -0.370, 95% CI = [-0.509, -0.231], p = 1.857 x 10^-7), but not by age (β= 0.049, 95% CI = [-0.090, 0.187], p = 0.490). Note that age and head motion for functional scans were not significantly related (r_s = -0.112, p = 0.137). When repeated for the baseline scans of NKI, alignment with the principal structural gradient was not significantly predicted by either scan age (β = 0.019, 95% CI = [-0.124, 0.163], p = 0.792) or head motion (β = -0.133, 95% CI = [-0.175, 0.009], p = 0.067) together in a single model, where age and motion were negatively correlated (r_s = -0.355, p < 0.001). Alignment with the principal functional gradient was significantly predicted by head motion (β = -0.183, 95% CI = [-0.329, -0.036], p = 0.014) but not by age (β= 0.066, 95% CI = [-0.081, 0.213], p = 0.377), where age and motion were also negatively correlated (r_s = -0.412, p < 0.001). Across modalities and datasets, alignment with the principal functional gradient in NKI was the only example in which there was a significant correlation between alignment and age (r_s = 0.164, p = 0.017) before accounting for head motion and sex. This suggests that apparent developmental effects on alignment are minimal, and where they do exist they are removed after accounting for head motion. Put together this suggests that the lack of order swapping for the first two gradients is not the result of the Procrustes rotation – even without the rotation there is no evidence for swapping”.

“To emphasise the importance of head motion in the appearance of developmental change in alignment, we examined whether accounting for head motion removes any apparent developmental change within NKI. Specifically, we tested whether head motion mediates the relationship between age and alignment (Figure 1X), controlling for sex, given that higher motion is associated with younger children (β= -0.429, 95% CI = [0.552, -0.305], p = 7.957 x 10^-11), and stronger alignment is associated with reduced motion (β = -0.211, 95% CI = [-0.344, -0.078], p = 2.017 x 10^-3). Motion mediated the relationship between age and alignment (β = 0.078, 95% CI = [0.006, 0.146], p = 1.200 x 10^-2), accounting for 38.5% variance in the age-alignment relationship, such that the link between age and alignment became non-significant after accounting for motion (β = 0.066, 95% CI = [-0.081, 0.214], p = 0.378). This firstly confirms our GLM analyses, where we control for motion and find no age associations. Moreover, this suggests that caution is required when associations between age and gradients are observed. In our analyses, because we calculate individual gradients, we can correct for individual differences in head motion in all our analyses. However, other than using an absolute motion threshold and motion-matched child and adolescent groups, individual differences in motion were not accounted for by prior work which demonstrated a flipping of the principal functional gradients with age (Dong et al., 2021)”. 

We further clarify the use of Procrustes rotation as a separate sub-section within the Methods (Page 25, Line 1273):

“Procrustes Rotation

For group-level analysis, for each hemisphere we constructed an affinity matrix using a normalized angle kernel and applied diffusion-map embedding. The left hemisphere was then aligned to the right using a Procrustes rotation. For individual-level analysis, eigenvectors for the left hemisphere were aligned with the corresponding group-level rotated eigenvectors. No alignment was applied across datasets. The only exception to this was for structural gradients derived from the referred CALM cohort. Specifically, we aligned the principal gradient of the left hemisphere to the secondary gradient of the right hemisphere: this was due to the first and second gradients explaining a very similar amount of variance, and hence their order was switched”. 

SC-FC Coupling Metric: The approach used to quantify nodal SC-FC coupling in this study appears to deviate from previously established methods in the field. The manuscript describes coupling as the "Spearman-rank correlation between Euclidean distances between each node and all others within structural and functional manifolds," but this description is unclear and lacks sufficient detail. Furthermore, this differs from what is typically referred to as SC-FC coupling in the literature. For instance, the cited study by Park et al. (2022) utilizes a multiple linear regression framework, where communicability, Euclidean distance, and shortest path length are independent variables predicting functional connectivity (FC), with the adjusted R-squared score serving as the coupling index for each node. On the other hand, the Baum et al. (2020) study, also cited, uses Spearman correlation, but between raw structural connectivity (SC) and FC values. If the authors opt to introduce a novel coupling metric, it is essential to demonstrate its similarity to these previous indices. I recommend providing an analysis (supplementary) showing the correlation between their chosen metric and those used in previous studies (e.g., the adjusted R-squared scores from Park et al. or the SC-FC correlation from Baum et al.). Furthermore, if the metrics are not similar and results are sensitive to this alternative metric, it raises concerns about the robustness of the findings. A sensitivity analysis would therefore be helpful (in case the novel coupling metric is not like previous ones) to determine whether the reported effects hold true across different coupling indices.

This is a great point, and we are happy to take the reviewer’s recommendation. There are multiple different ways of calculating structure-function coupling. For our set of questions, it was important that our metric incorporated information about the structural and functional manifolds, rather than being a separate approach that is unrelated to these low-dimensional embeddings. Put simply, we wanted our coupling measure to be about the manifolds and gradients outlined in the early sections of the results. We note that the multiple linear regression framework was developed by Vázquez-Rodríguez and colleagues (2019), whilst the structure-function coupling computed in manifold space by Park and colleagues (2022) was operationalised as a linear correlation between z-transformed functional connectomes and structural differentiation eigenvectors. To clarify how this coupling was calculated, and to justify why we developed a new coupling method based on manifolds rather than borrow an existing approach from the literature, we have revised the manuscript to make this far clearer for readers (Page 13, line 604):

“To examine the relationship between each node’s relative position in structural and functional manifold space, we turned our attention to structure-function coupling. Whilst prior work typically computed coupling using raw streamline counts and functional connectivity matrices, either as a correlation (Baum et al., 2020) or through a multiple linear regression framework (Vázquez-Rodríguez et al., 2019), we opted to directly incorporate low-dimensional embeddings within our coupling framework. Specifically, as opposed to correlating row-wise raw functional connectivity with structural connectivity eigenvectors (Park et al., 2022), our metric directly incorporates the relative position of each node in low-dimensional structural and functional manifold spaces. Each node was situated in a low-dimensional 3D space, the axes of which were each participant’s gradients, specific to each modality. For each participant and each node, we computed the Euclidean distance with all other nodes within structural and functional manifolds separately, producing a vector of size 200 x 1 per modality. The nodal coupling coefficient was the Spearman correlation between each node’s Euclidean distance to all other nodes in structural manifold space, and that in functional manifold space. Put simply, a strong nodal coupling coefficient suggests that that node occupies a similar location in structural space, relative to all other nodes, as it does in functional space”. 

We also agree with the reviewer’s recommendation to compare this to some of the more standard ways of calculating coupling. We compare our metric with 3 others (Baum et al., 2020; Park et al., 2022; VázquezRodríguez et al., 2019), and find that all metrics capture the core developmental sensorimotor-to-association axis (Sydnor et al., 2021). Interestingly, manifold-based coupling measures captured this axis more strongly than non-manifold measures. We have updated the Results accordingly (Page 14, Line 638):

“To evaluate our novel coupling metric, we compared its cortical spatial distribution to three others (Baum et al., 2020; Park et al., 2022; Vázquez-Rodríguez et al., 2019), using the group-level thresholded structural and functional connectomes from the referred CALM cohort. As shown in Figure 4c, our novel metric was moderately positively correlated to that of a multi-linear regression framework (r_s = 0.494, p_spin = 0.004; Vázquez-Rodríguez et al., 2019) and nodal correlations of streamline counts and functional connectivity (r_s = 0.470, p_spin = 0.005; Baum et al., 2020). As expected, our novel metric was strongly positively correlated to the manifold-derived coupling measure (r_s = 0.661, p_spin < 0.001; Park et al., 2022), more so than the first (Z(198) = 3.669, p < 0.001) and second measure (Z(198) = 4.012, p < 0.001). Structure-function coupling is thought to be patterned along a sensorimotor-association axis (Sydnor et al., 2021): all four metrics displayed weak-tomoderate alignment (Figure 4c). Interestingly, the manifold-based measures appeared most strongly aligned with the sensorimotor-association axis: the novel metric was more strongly aligned than the multi-linear regression framework (Z(198) = -11.564, p < 0.001) and the raw connectomic nodal correlation approach (Z(198) = -10.724, p < 0.001), but the previously-implemented structural manifold approach was more strongly aligned than the novel metric  (Z(198) = -12.242, p < 0.001). This suggests that our novel metric exhibits the expected spatial distribution of structure-function coupling, and the manifold approach more accurately recapitulates the sensorimotor-association axis than approaches based on raw connectomic measures”.

We also added the following to the legend of Figure 4 on page 15:

“d. The inset Spearman correlation plot of the 4 coupling measures shows moderate-to-strong correlations (p_spin < 0.005 for all spatial correlations). The accompanying lollypop plot shows the alignment between the sensorimotor-to-association axis and each of the 4 coupling measures, with the novel measure coloured in light purple (p_spin < 0.007 for all spatial correlations)”. 

Prediction vs. Association Analysis: The term “prediction” is used throughout the manuscript to describe what appear to be in-sample association tests. This terminology may be misleading, as prediction generally implies an out-of-sample evaluation where models trained on a subset of data are tested on a separate, unseen dataset. If the goal of the analyses is to assess associations rather than make true predictions, I recommend refraining from the term “prediction” and instead clarifying the nature of the analysis. Alternatively, if prediction is indeed the intended aim (which would be more compelling), I suggest conducting the evaluations using a k-fold cross-validation framework. This would involve training the Generalized Additive Mixed Models (GAMMs) on a portion of the data and training their predictive accuracy on a held-out sample (i.e. different individuals). Additionally, the current design appears to focus on predicting SC-FC coupling using cognitive or pathological dimensions. This is contrary to the more conventional approach of predicting behavioural or pathological outcomes from brain markers like coupling. Could the authors clarify why this reverse direction of analysis was chosen? Understanding this choice is crucial, as it impacts the interpretation and potential implications of the findings. 

We have replaced “prediction” with “association” across the manuscript. However, for analyses corresponding to Figure 5, which we believe to be the most compelling, we conducted a stratified 5-fold cross-validation procedure, outlined below, repeated 100 times to account for random variation in the train-test splits. To assess whether prediction accuracy in the test splits was significantly greater than chance, we compared our results to those derived from a null dataset in which cognitive factor 2 scores had been permuted across participants. To account for the time-series element and block design of our data, in that some participants had 2 or more observations, we permuted entire participant blocks of cognitive factor 2 scores, keeping all other variables, including covariates, the same. Included in our manuscript are methodological details and results pertaining to this procedure. Specifically, the following has been added to the Results (Page 16, Line 758):

“To examine the predictive value of the second cognitive factor for global and network-level structure-function coupling, operationalised as a Spearman rank correlation coefficient, we implemented a stratified 5-fold crossvalidation framework, and predictive accuracy compared with that of a null data frame with cognitive factor 2 scores permuted across participant blocks (see ‘GAMM cross-validation’ in the Methods). This procedure was repeated 100 times to account for randomness in the train-test splits, using the same model specification as above. Therefore, for each of the 5 network partitions in which an interaction between the second cognitive factor and age was a significant predictor of structure-function coupling (global, visual, somato-motor, dorsal attention, and default-mode), we conducted a Welch’s independent-sample t-test to compare 500 empirical prediction accuracies with 500 null prediction accuracies. Across all 5 network partitions, predictive accuracy of coupling was significantly higher than that of models trained on permuted cognitive factor 2 scores (all p < 0.001). We observed the largest difference between empirical (M = 0.029, SD = 0.076) and null (M = -0.052, SD = 0.087) prediction accuracy in the somato-motor network [t (980.791) = 15.748, p < 0.001, Cohen’s d = 0.996], and the smallest difference between empirical (M = 0.080, SD = 0.082) and null (M = 0.047, SD = 0.081) prediction accuracy in the dorsal attention network [t (997.720) = 6.378, p < 0.001, Cohen’s d = 0.403]. To compare relative prediction accuracies, we ordered networks by descending mean accuracy and conducted a series of Welch’s independent sample t-tests, followed by FDR correction (Figure 5X). Prediction accuracy was highest in the default-mode network (M = 0.265, SD = 0.085), two-fold that of global coupling (t(992.824) = 25.777, p_FDR = 5.457 x 10^-112, Cohen’s d = 1.630, M = 0.131, SD = 0.079). Global prediction accuracy was significantly higher than the visual network (t (992.644) = 9.273, p_FDR = 1.462 x 10^-19, Cohen’s d = 0.586, M = 0.083, SD = 0.085), but visual prediction accuracy was not significantly higher than within the dorsal attention network (t (997.064) = 0.554, p_FDR = 0.580, Cohen’s d = 0.035, M = 0.080, SD = 0.082). Finally, prediction accuracy within the dorsal attention network was significantly stronger than that of the somato-motor network [t (991.566) = 10.158, p_FDR = 7.879 x 10^-23, Cohen’s d = 0.642 M = 0.029, SD = 0.076]. Together, this suggests that out-of-sample developmental predictive accuracy for structure-function coupling, using the second cognitive factor, is strongest in the higher-order default-mode network, and lowest in the lower-order somatosensory network”. 

We have added a separate section for GAMM cross-validation in the Methods (Page 27, Line 1361):

GAMM cross-validation

“We implemented a 5-fold cross validation procedure, stratified by dataset (2 levels: CALM or NKI). All observations from any given participant were assigned to either the testing or training fold, to prevent data leakage, and the cross-validation procedure was repeated 100 times, to account for randomness in data splits. The outcome was predicted global or network-level structure-function coupling across all test splits, operationalised as the Spearman rank correlation coefficient. To assess whether prediction accuracy exceeded chance, we compared empirical prediction accuracy with that of GAMMs trained and tested on null data in which cognitive factor 2 scores were permuted across subjects. The number of observations formed 3 exchangeability blocks (N = 320 with one observation, N = 105 with two observations, and N = 33 with three observations), whereby scores from a participant with two observations were replaced by scores from another participant with two observations, with participant-level scores kept together, and so on for all numbers of observations. We compared empirical and null prediction accuracies using independent sample t-tests as, although the same participants were examined, the shuffling meant that the relative ordering of participants within both distributions was not preserved. For parallelisation and better stability when estimating models fit on permuted data, we used the bam function from the mgcv R package (Wood, 2017)”. 

We also added a justification for why we predicted coupling using behaviour or psychopathology, rather than vice versa (Page 27, Line 1349):

“When using our GAMMs to test for the relationship between cognition and psychopathology and our coupling metrics, we opted to predict structure-function coupling using cognitive or psychopathological dimensions, rather than vice versa, to minimise multiple comparisons. In the current framework, we corrected for 8 multiple comparisons within each domain. This would have increased to 16 multiple comparison corrections for predicting two cognitive dimensions using network-level coupling, and 24 multiple comparison corrections for predicting three psychopathology dimensions. Incorporating multiple networks as predictors within the same regression framework introduces collinearity, whilst the behavioural dimensions were orthogonal: for example, coupling is strongly correlated between the somato-motor and ventral attention networks (r_s = 0.721), between the default-mode and frontoparietal networks (r_s = 0.670), and between the dorsal attention and fronto-parietal networks (r_s = 0.650)”. 

Finally, we noticed a rounding error in the ages of the data frame containing the structure-function coupling values and the cognitive/psychopathology dimensions. We rectified this and replaced the GAMM results, which largely remained the same. 

In typical applications of diffusion map embedding, sparsification (e.g., retaining only the top 10  of the strongest connections) is often employed at the vertex-level resolution to ensure computational feasibility. However, since the present study performs the embedding at the level of 200 brain regions (a considerably coarser resolution), this step may not be necessary or justifiable. Specifically, for FC, it might be more appropriate to retain all positive connections rather than applying sparsification, which could inadvertently eliminate valuable information about lower-strength connections. Whereas for SC, as the values are strictly non-negative, retaining all connections should be feasible and would provide a more complete representation of the structural connectivity patterns. Given this, it would be helpful if the authors could clarify why they chose to include sparsification despite the coarser regional resolution, and whether they considered this alternative approach (using all available positive connections for FC and all non-zero values for SC). It would be interesting if the authors could provide their thoughts on whether the decision to run evaluations at the resolution of brain regions could itself impact the functional and structural manifolds, their alteration with age, and or their stability (in contrast to Dong et al. which tested alterations in highresolution gradients).

This is another great point. We could retain all connections, but we usually implement some form of sparsification to reduce noise, particularly in the case of functional connectivity. But we nonetheless agree with the reviewer’s point. We should check what impact this is having on the analysis. In brief, we found minimal effects of thresholding, suggesting that the strongest connections are driving the gradient (Page 7, Line 304):

“To assess the effect of sparsity on the derived gradients, we examined group-level structural (N = 222) and functional (N = 213) connectomes from the baseline session of NKI. The first three functional connectivity gradients derived using the full connectivity matrix (density = 92%) were highly consistent with those obtained from retaining the strongest 10% of connections in each row (r₁ = 0.999, r₂ = 0.998, r₃ < 0.999, all p < 0.001). Likewise, the first three communicability gradients derived from retaining all streamline counts (density = 83%) were almost identical to those obtained from 10% row-wise thresholding (r₁ = 0.994, r₂ = 0.963, r₃ = 0.955, all p < 0.001). This suggests that the reported gradients are driven by the strongest or most consistent connections within the connectomes, with minimal additional information provided by weaker connections. In terms of functional connectivity, such consistency reinforces past work demonstrating that the sensorimotor-toassociation axis, the major axis within the principal functional connectivity gradient, emerges across both the top- and bottom-ranked functional connections (Nenning et al., 2023)”.

Furthermore, we appreciate the nudge to share our thoughts on whether the difference between vertex versus nodal metrics could be important here, particularly regarding thresholds. To combine this point with R2’s recommendation to expand the Discussion, we have added the following paragraph (Page 19, Line 861): 

“We consider the role of thresholding, cortical resolution, and head motion as avenues to reconcile the present results with select reports in the literature (Dong et al., 2021; Xia et al., 2022). We would suggest that thresholding has a greater effect on vertex-level data, rather than parcel-level. For example, a recent study revealed that the emergence of principal vertex-level functional connectivity gradients in childhood and adolescence are indeed threshold-dependent (Dong et al., 2024). Specifically, the characteristic unimodal organisation for children and transmodal organisation for adolescents only emerged at the 90% threshold: a 95% threshold produced a unimodal organisation in both groups, whilst an 85% threshold produced a transmodal organisation in both groups. Put simply, the ‘swapping’ of gradient orders only occurs at certain thresholds. Furthermore, our results are not necessarily contradictory to this prior report (Dong et al., 2021): developmental changes in high-resolution gradients may be supported by a stable low-dimensional coarse manifold. Indeed, our decision to use parcellated connectomes was partly driven by recent work which demonstrated that vertex-level functional gradients may be derived using biologically-plausible but random data with sufficient spatial smoothing, whilst this effect is minimal at coarser resolutions (Watson & Andrews, 2023). We observed a gradual increase in the variance of individual connectomes accounted for by the principal functional connectivity gradient in the referred subset of CALM, in line with prior vertex-level work demonstrating a gradual emergence of the sensorimotor-association axis as the principal axis of connectivity (Xia et al., 2022), as opposed to a sudden shift. It is also possible that vertex-level data is more prone to motion artefacts in the context of developmental work. Transitioning from vertex-level to parcel-level data involves smoothing over short-range connectivity, thus greater variability in short-range connectivity can be observed in vertex-level data. However, motion artefacts are known to increase short-range connectivity and decrease long-range connectivity, mimicking developmental changes (Satterthwaite et al., 2013). Thus, whilst vertexlevel data offers greater spatial resolution in representation of short-range connectivity relative to parcel-level data, it is possible that this may come at the cost of making our estimates of the gradients more prone to motion”.

Evaluating the consistency of gradients across development: the results shown in Figure 1e are used as evidence suggesting that gradients are consistent across ages. However, I believe additional analyses are required to identify potential sources of the observed inconsistency compared to previous works. The claim that the principal gradient explains a similar degree of variance across ages does not necessarily imply that the spatial structure remains the same. The observed variance explanation is hence not enough to ascertain inconsistency with findings from Dong et al., as the spatial configuration of gradients may still change over time. I suggest the following additional analyses to strengthen this claim. Alignment to group-level gradients: Assess how much of the variance in individual FC matrices is explained by each of the group-level gradients (G1, G2, and G3, for both FC and SC). This analysis could be visualized similarly to Figure 1e, with age on the x-axis and variance explained on the y-axis. If the explained variance varies as a function of age, it may indicate that the gradients are not as consistent as currently suggested. 

This is another great suggestion. In the additional analyses above (new group-level analyses and unrotated gradient analyses) we rule-out a couple of the potential causes of the different developmental trends we observe in our data – namely the stability of the gradients over time. The suggested additional analysis is a great idea, and we have implemented it as follows (Page 8, Line 363):

“To evaluate the consistency of gradients across development, across baseline participants with functional connectomes from the referred CALM cohort (N = 177), we calculated the proportion of variance in individuallevel connectomes accounted for by group-level functional gradients. Specifically, we calculated the proportion of variance in an adjacency matrix A accounted for by the vector v_i as the fraction of the square of the scalar projection of v_i onto A, over the Frobenius norm of A. Using a generalised linear model, we then tested whether the proportion of variance explained varies systematically with age, controlling for sex and headmotion. The variance in individual-level functional connectomes accounted for by the group-level principal functional gradient gradually increased with development (β= 0.111, 95% CI = [0.022, 0.199], p = 1.452 x 10^-2, Cohen’s d = 0.367), as shown in Figure 1g, and decreased with higher head motion ( β = -10.041, 95% CI = [12.379, -7.702], p = 3.900 x 10^-17), with no effect of sex (β= 0.071, 95% CI = [-0.380, 0.523], p = 0.757). We observed no developmental effects on the variance explained by the second (r_s = 0.112, p = 0.139) or third (r_s = 0.053, p = 0.482) group-level functional gradient. When repeated with the baseline functional connectivity for NKI (N = 213), we observed no developmental effects (β = 0.097, 95% CI = [-0.035, 0.228], p = 0.150) on the variance explained by the principal functional gradient after accounting for motion (β= -3.376, 95% CI = [8.281, 1.528], p = 0.177) and sex (β = -0.368, 95% CI = [-1.078, 0.342], p = 0.309). However, we observed significant developmental correlations between age and variance (r_s = 0.137, p = 0.046) explained before accounting for head motion and sex. We observed no developmental effects on the variance explained by the second functional gradient (r_s = -0.066, p = 0.338), but a weak negative developmental effect on the variance explained by the third functional gradient (r_s = -0.189, p = 0.006). Note, however, the magnitude of the variance accounted for by the third functional gradient was very small (all < 1%). When applied to communicability matrices in CALM, the proportion of variance accounted for by the group-level communicability gradient was negligible (all < 1%), precluding analysis of developmental change”. 

“To further probe the consistency of gradients across development, we examined developmental changes in the standard deviation of gradient values, corresponding to heterogeneity, following prior work examining morphological (He et al., 2025) and functional connectivity gradients (Xia et al., 2022). Using a series of generalised linear models within the baseline referred subset of CALM, correcting for head motion and sex, we found that gradient variation for the principal functional gradient increased across development (= 0.219, 95% CI = [0.091, 0.347], p = 0.001, Cohen’s d = 0.504), indicating greater heterogeneity (Figure 1h), whilst gradient variation for the principal communicability gradient decreased across development (β = -0.154, 95% CI = [-0.267, -0.040], p = 0.008, Cohen’s d = -0.301), indicating greater homogeneity (Figure 1h). Note, a paired t-test on the 173 common participants demonstrated a significant effect of modality on gradient variability (t(172) = -56.639, p = 3.663 x 10^-113), such that the mean variability of communicability gradients (M = 0.033, SD = 0.001) was less than half that of functional connectivity (M = 0.076, SD = 0.010). Together, this suggests that principal functional connectivity and communicability gradients are established early in childhood and display age-related refinement, but not replacement”. 

The Issue of Abstraction and Benefits of the Gradient-Based View: The manuscript interprets the eccentricity findings as reflecting changes along the segregation-integration spectrum. Given this, it is unclear why a more straightforward analysis using established graph-theory metrics of segregationintegration was not pursued instead. Mapping gradients and computing eccentricity adds layers of abstraction and complexity. If similar interpretations can be derived directly from simpler graph metrics, what additional insights does the gradient-based framework offer? While the manuscript argues that this approach provides “a more unifying account of cortical reorganization”, it is not evident why this abstraction is necessary or advantageous over traditional graph metrics. Clarifying these benefits would strengthen the rationale for using this method. 

This is a great point, and something we spent quite a bit of time considering when designing the analysis. The central goal of our project was to identify gradients of brain organisation across different datasets and modalities and then test how the organisational principles of those modalities align. In other words, how do structural and functional ‘spaces’ intersect, and does this vary across the cortex? That for us was the primary motivation for operationalising organisation as nodal location within a low-dimensional manifold space (Bethlehem et al., 2020; Gale et al., 2022; Park et al., 2021), using a simple composite measure to achieve compression, rather than as a series of graph metrics. The reason we subsequently calculated those graph metrics and tested for their association was simply to help us interpret what eccentricity within that lowdimensional space means. Manifold eccentricity was moderately positively correlated to graph-theory metrics of integration, leaving a substantial portion of variance unaccounted for, but that association we think is nonetheless helpful for readers trying to interpret eccentricity. However, since ME tells us about the relative position of a node in that low-dimensional space, it is also likely capturing elements of multiple graph theory measures. Following the Reviewer’s question, this is something we decided to test. Specifically, using 4 measures of segregation, including two new metrics requested by the Reviewer in a minor point (weighted clustering coefficient and normalized degree centrality), we conducted a dominance analysis (Budescu, 1993) with normalized manifold eccentricity of the group-level referred CALM structural connectome. We also detail the use of gradient measures in developmental contexts, and how they can be complementary to traditional graph theory metrics. 

We have added the following to the Results section (Page 10, Lines 472 onwards): 

“To further contextualise manifold eccentricity in terms of integration and segregation beyond simple correlations, we conducted a multivariate dominance analysis (Budescu, 1993) of four graph theory metrics of segregation as predictors of nodal normalized manifold eccentricity within the group-level referred CALM structural and functional connectomes (Figure 2c). A dominance analysis assesses the relative importance of each predictor in a multilinear regression framework by fitting 2ⁿ – 1 models (where n is the number of predictors) and calculating the relative increase in adjusted R2 caused by adding each predictor to the model across both main effects and interactions. A multilinear regression model including weighted clustering coefficient, within-module degree Z-score, participation coefficient and normalized degree centrality accounted for 59% of variance in nodal manifold eccentricity in the group-level CALM structural connectome. Withinmodule degree Z score was the most important predictor (40.31% dominance), almost twice that of the participation coefficient (24.03% dominance) and normalized degree centrality (24.05% dominance) which made roughly equal contributions. The least important predictor was the weighted clustering coefficient (11.62% dominance). When the same approach was applied for the group-level referred CALM functional connectome, the 4 predictors accounted for 52% variability. However, in contrast to the structural connectome, functional manifold eccentricity seemed to incorporate the same graph theory metrics in different proportions. Normalized degree centrality was the most important predictor (47.41% dominance), followed by withinmodule degree Z-score (24.27%), and then the participation coefficient (15.57%) and weighted clustering coefficient (12.76%) which made approximately equal contributions. Thus, whilst structural manifold eccentricity was dominated most by within-module degree Z-score and least by the weighted clustering coefficient, functional manifold eccentricity was dominated most by normalized degree centrality and least by the weighted clustering coefficient. This suggests that manifold mapping techniques incorporate different aspects of integration dependent on modality. Together, manifold eccentricity acts as a composite measure of segregation, being differentially sensitive to different aspects of segregation, without necessitating a priori specification of graph theory metrics. Further discussion of the value of gradient-based metrics in developmental contexts and as a supplement to traditional graph theory analyses is provided in the ‘Manifold Eccentricity’ methodology sub-section”. 

We added further justification to the manifold eccentricity Methods subsection (Page 26, line 1283):

“Gradient-based measures hold value in developmental contexts, above and beyond traditional graph theory metrics: within a sample of over 600 cognitively-healthy adults aged between 18 and 88 years old, sensitivity of gradient-based within-network functional dispersion to age were stronger and more consistent across networks compared to segregation (Bethlehem et al., 2020). In the context of microstructural profile covariance, modules resolved by Louvain community detection occupied distinct positions across the principal two gradients, suggesting that gradients offer a way to meaningfully order discrete graph theory analyses (Paquola et al., 2019)”. 

We added the following to the Introduction section outlining the application of gradients as cortex-wide coordinate systems (Page 3, Line 121):

“Using the gradient-based approach as a compression tool, thus forgoing the need to specify singular graph theory metrics a priori, we operationalised individual variability in low-dimensional manifolds as eccentricity (Gale et al., 2022; Park et al., 2021). Crucially, such gradients appear to be useful predictors of phenotypic variation, exceeding edge-level connectomics. For example, in the case of functional connectivity gradients, their predictive ability for externalizing symptoms and general cognition in neurotypical adults surpassed that of edge-level connectome-based predictive modelling (Hong et al., 2020), suggesting that capturing lowdimensional manifolds may be particularly powerful biomarkers of psychopathology and cognition”. 

We also added the following to the Discussion section (Page 18, Line 839):

“By capitalising on manifold eccentricity as a composite measure of segregation across development, we build upon an emerging literature pioneering gradients as a method to establish underlying principles of structural (Paquola et al., 2020; Park et al., 2021) and functional (Dong et al., 2021; Margulies et al., 2016; Xia et al., 2022) brain development without a priori specification of specific graph theory metrics of interest”. 

It is unclear whether the statistical tests finding significant dataset effects are capturing effects of neurotypical vs. Neurodivergent, or simply different scanners/sites. Could the neurotypical portion of CALM also be added to distinguish between these two sources of variability affecting dataset effects (i.e. ideally separating this to the effect of site vs. neurotypicality would better distinguish the effect of neurodivergence).

At a group-level, differences in the gradients between the two cohorts are very minor. Indeed, in the manuscript we describe these gradients as being seemingly ‘universal’. But we agree that we should test whether we can directly attribute any simple main effects of ‘dataset’ are resulting from the different site or the phenotype of the participants. The neurotypical portion of CALM (collected at the same site on the same scanner) helped us show that any minor differences in the gradient alignments is likely due to the site/scanner differences rather than the phenotype of the participants. We took the same approach for testing the simple main effects of dataset on manifold eccentricity. To better parse neurotypicality and site effects at an individual-level, we conducted a series of sensitivity analyses. First, in response to the reviewer’s earlier comment, we conducted a series of nodal generalized linear models for communicability and FC gradients derived from neurotypical and neurodivergent portions of CALM, alongside NKI, and tested for an effect of neurotypicality above and beyond scanner. As at the group level, having those additional scans on a ‘comparison’ sample for CALM is very helpful in teasing apart these effects. We find that neurotypicality affects communicability gradient expression to a greater degree than functional connectivity. We visualised these results and added them to Figure 1. Second, we used the same approach but for manifold eccentricity. Again, we demonstrate greater sensitivity of neurotypicality to communicability at a global-level, but we cannot pin these effects down to specific networks because the effects do not survive the necessary multiple comparison correction. We have added these analyses to the manuscript (Page 13, Line 583): 

“Much as with the gradients themselves, we suspected that much of the simple main effect of dataset could reflect the scanner / site, rather than the difference in phenotype. Again, we drew upon the CALM comparison children to help us disentangle these two explanations. As a sensitivity analysis to parse effects of neurotypicality and dataset on manifold eccentricity, we conducted a series of generalized linear models predicting mean global and network-level manifold eccentricity, for each modality. We did this across all the baseline data (i.e. including the neurotypical comparison sample for CALM) using neurotypicality (2 levels: neurodivergent or neurotypical), site (2 levels: CALM or NKI), sex, head motion, and age at scan (Figure 3X). We restricted our analysis to baseline scans to create more equally-balanced groups. In terms of structural manifold eccentricity (N = 313 neurotypical, N = 311 neurodivergent), we observed higher manifold eccentricity in the neurodivergent participants at a global level (β = 0.090, p = 0.019, Cohen’s d = 0.188) but the individual network level effects did not survive the multiple comparison correction necessary for looking across all seven networks, with the default-mode network being the strongest (β = 0.135, p = 0.027, p_FDR = 0.109, Cohen’s d = 0.177). There was no significant effect of neurodiversity on functional manifold eccentricity (N = 292 neurotypical and N = 177 neurodivergent). This suggests that neurodiversity is significantly associated with structural manifold eccentricity, over and above differences in site, but we cannot distinguish these effects reliably in the functional manifold data”. 

Third, we removed the Scheirer-Ray-Hare test from the results for two reasons. First, its initial implementation did not account for repeated measures, and therefore non-independence between observations, as the same participants may have contributed both structural and functional data. Second, if we wanted to repeat this analysis in CALM using the referred and control portions, a significant difference in group size existed, which may affect the measures of variability. Specifically, for baseline CALM, 311 referred and 91 control participants contributed SC data, whilst 177 referred and 79 control participants contributed FC data. We believe that the ‘cleanest’ parsing of dataset and site for effects of eccentricity is achieved using the GLMs in Figure 3. 

We observed no significant effect of neurodivergence on the magnitude of structure-function coupling across development, and have added the following text (Page 14, Line 632):

“To parse effects of neurotypicality and dataset on structure-function coupling, we conducted a series of generalized linear models predicting mean global and network-level coupling using neurotypicality, site, sex, head motion, and age at scan, at baseline (N = 77 CALM neurotypical, N = 173 CALM neurodivergent, and N = 170 NKI). However, we found no significant effects of neurotypicality on structure-function coupling across development”. 

Since we demonstrated no significant effects of neurotypicality on structure-function coupling magnitude across development, but found differential dataset-specific effects of age on coupling development, we added the following sentence at the end of the coupling trajectory results sub-section (Page 14, line 664):

“Together, these effects demonstrate that whilst the magnitude of structure-function coupling appears not to be sensitive to neurodevelopmental phenotype, its development with age is, particularly in higher-order association networks, with developmental change being reduced in the neurodivergent sample”.  

Figure 1.c: A non-parametric permutation test (e.g. Mann-Whitney U test) could quantitatively identify regions with significant group differences in nodal gradient values, providing additional support for the qualitative findings.

This is a great idea. To examine the effect of referral status on nodal gradient values, whilst controlling for covariates (head motion and sex), we conducted a series of generalised linear models. We opted for this instead of a Mann-Whitney U test, as the former tests for differences in distributions, whilst the direction of the t-statistic for referral status from the GLM would allow us to specify the magnitude and direction of differences in nodal gradient values between the two groups. Again, we conducted this in CALM (referred vs control), at an individual-level, as downstream analyses suggested a main effect of dataset (which is reflected in the highly-similar group-level referred and control CALM gradients). We have updated the Results section with the following text (Page 6, Line 283):

“To examine the effect of referral status on participant-level nodal gradient values in CALM, we conducted a series of generalized linear models controlling for head motion, sex and age at scan (Figure 1d). We restricted our analyses to baseline scans to reduce the difference in sample size for the referred (311 communicability and 177 functional gradients, respectively) and control participants (91 communicability and 79 functional gradients, respectively), and to the principal gradients. For communicability, 42 regions showed a significant effect (p < 0.05) of neurodivergence before FDR correction, with 9 post FDR correction. 8 of these 9 regions had negative t-statistics, suggesting a reduced nodal gradient value and representation in the neurodivergent children, encompassing both lower-order somatosensory cortices alongside higher-order fronto-parietal and default-mode networks. The largest reductions were observed within the prefrontal cortices of the defaultmode network (t = -3.992, p = 6.600 x 10^-5, p_FDR = 0.013, Cohen’s d = -0.476), the left orbitofrontal cortex of the limbic network (t = -3.710, p = 2.070 x 10^-4, p_FDR = 0.020, Cohen’s d = -0.442) and right somato-motor cortex (t = -3.612, p = 3.040 x 10^-4, p_FDR = 0.020, Cohen’s d = -0.431). The right visual cortex was the only exception, with stronger gradient representation within the neurotypical cohort (t = 3.071, p = 0.002, p_FDR = 0.048, Cohen’s d = 0.366). For functional connectivity, comparatively fewer regions exhibited a significant effect (p < 0.05) of neurotypicality, with 34 regions prior to FDR correction and 1 post. Significantly stronger gradient representation was observed in neurotypical children within the right precentral ventral division of the defaultmode network (t = 3.930, p = 8.500 x 10^-5, p_FDR = 0.017, Cohen’s d = 0.532). Together, this suggests that the strongest and most robust effects of neurodivergence are observed within gradients of communicability, rather than functional connectivity, where alterations in both affect higher-order associative regions”. 

In the harmonization methodology, it is mentioned that “if harmonisation was successful, we’d expect any significant effects of scanner type before harmonisation to be non-significant after harmonisation”. However, given that there were no significant effects before harmonization, the results reported do not help in evaluating the quality of harmonization.

We agree with the Reviewer, and have removed the post-harmonisation GLMs, and instead stating that there were no significant effects of scanner type before harmonization. 

Figure 3: It would be helpful to include a plot showing the GAMM predictions versus real observations of eccentricity (x-axis: predictions, y-axis: actual values). 

To plot the GAMM-predicted smooth effects of age, which we used for visualisation purposes only, we used the get_predictions function from the itsadug R package. This creates model predictions using the median value of nuisance covariates. Thus, whilst we specified the entire age range, the function automatically chooses the median of head motion, alongside controlling for sex (default level: male) and, for each dataset-specific trajectory. Since the gamm4 package separates the fitted model into a gam and linear mixed effects model (which accounts for participant ID as a random effect), and the get_predictions function only uses gam, random effects are not modelled in the predicted smooths. Therefore, any discrepancy between the observed and predicted manifold eccentricity values is likely due to sensitivity to default choices of covariates other than age, or random effects. To prevent Figure 3 being too over-crowded, we opted to not include the predictions: these were strongly correlated with real structural manifold data, but less for functional manifold data especially where significant developmental change was absent.

The 30mm threshold for filtering short streamlines in tractography is uncommon. What is the rationale for using such a large threshold, given the potential exclusion of many short-range association fibres?

A minimum length of 30mm was the default for the MRtrix3 reconstruction workflow, and something we have previously used. In a previous project, we systematically varied the minimum fibre length and found that this had minimal impact on network organisation (e.g. Mousley et al. 2025). However, we accept that short-range association fibres may have been excluded and have included this in the Discussion as a methodological limitation, alongside our predictions for how the gradients and structure-function coupling may’ve been altered had we included such fibres (Page 20, Line 955):

“A potential methodological limitation in the construction of structural connectomes was the 30mm tract length threshold which, despite being the QSIprep reconstruction default (Cieslak et al., 2021), may have potentially excluded short-range association fibres. This is pertinent as tracts of different lengths exhibit unique distributions across the cortex and functional roles (Bajada et al., 2019) : short-range connections occur throughout the cortex but peak within primary areas, including the primary visual, somato-motor, auditory, and para-hippocampal cortices, and are thought to dominate lower-order sensorimotor functional resting-state networks, whilst long-range connections are most abundant in tertiary association areas and are recruited alongside tracts of varying lengths within higher-order functional resting-state networks. Therefore, inclusion of short-range association fibres may have resulted in a relative increase in representation of lower-order primary areas and functional networks. On the other hand, we also note the potential misinterpretation of short-range fibres: they may be unreliably distinguished from null models in which tractography is restricted by cortical gyri only (Bajada et al., 2019). Further, prior (neonatal) work has demonstrated that the order of connectivity of regions and topological fingerprints are consistent across varying streamline thresholds (Mousley et al., 2025), suggesting minimal impact”. 

Given the spatial smoothing of fMRI data (6mm FWHM), it would be beneficial to apply connectome spatial smoothing to structural connectivity measures for consistent spatial smoothness.

This is an interesting suggestion but given we are looking at structural communicability within a parcellated network, we are not sure that it would make any difference. The data structural data are already very smooth. Nonetheless we have added the following text to the Discussion (Page 20, Line 968): 

“Given the spatial smoothing applied to the functional connectivity data, and examining its correspondence to streamline-count connectomes through structure-function coupling, applying the equivalent smoothing to structural connectomes may improve the reliability of inference, and subsequent sensitivity to cognition and psychopathology. Connectome spatial smoothing involves applying a smoothing kernel to the two streamline endpoints, whereby variations in smoothing kernels are selected to optimise the trade-off between subjectlevel reliability and identifiability, thus increasing the signal-to-noise ratio and the reliability of statistical inferences of brain-behaviour relationships (Mansour et al., 2022). However, we note that such smoothing is more effective for high-resolution connectomes, rather than parcel-level, and so have only made a modest improvement (Mansour et al., 2022)”.

Why was harmonization performed only within the CALM dataset and not across both CALM and NKI datasets? What was the rationale for this decision?

We thought about this very carefully. Harmonization aims to remove scanner or site effects, whilst retaining the crucial characteristics of interest. Our capacity to retain those characteristics is entirely dependent on them being *fully* captured by covariates, which are then incorporated into the harmonization process. Even with the best set of measures, the idea that we can fully capture ‘neurodivergence’ and thus preserve it in the harmonisation process is dubious. Indeed, across CALM and NKI there are limited number of common measures (i.e. not the best set of common measures), and thus we are limited in our ability to fully capture the neurodivergence with covariates. So, we worried that if we put these two very different datasets into the harmonisation process we would essentially eliminate the interesting differences between the datasets. We have added this text to the harmonization section of the Methods (Page 24, Line 1225):

“Harmonization aims to retain key characteristics of interest whilst removing scanner or site effects. However, the site effects in the current study are confounded with neurodivergence, and it is unlikely that neurodivergence may be captured fully using common covariates across CALM and NKI. Therefore, to preserve variation in neurodivergence, whilst reducing scanner effects, we harmonized within the CALM dataset only”. 

The exclusion of subcortical areas from connectivity analyses is not justified. 

This is a good point. We used the Schaefer atlas because we had previously used this to derive both functional and structural connectomes, but we agree that it would have been good to include subcortical areas (Page 20, Line 977). 

“A potential limitation of our study was the exclusion of subcortical regions. However, prior work has shed light on the role of subcortical connectivity in structural and functional gradients, respectively, of neurotypical populations of children and adolescents (Park et al., 2021; Xia et al., 2022). For example, in the context of the primary-to-transmodal and sensorimotor-to-visual functional connectivity gradients, the mean gradient scores within subcortical networks were demonstrated to be relatively stable across childhood and adolescence (Xia et al., 2022). In the context of structural connectivity gradients derived from streamline counts, which we demonstrated were highly consistent with those derived from communicability, subcortical structural manifolds weighted by their cortical connectivity were anchored by the caudate and thalamus at one pole, and by the hippocampus and nucleus accumbens at the opposite pole, with significant age-related manifold expansion within the caudate and thalamus (Park et al., 2021)”. 

In the KNN imputation method, were uniform weights used, or was an inverse distance weighting applied?

Uniform weights were used, and we have updated the manuscript appropriately.

The manuscript should clarify from the outset that the reported sample size (N) includes multiple longitudinal observations from the same individuals and does not reflect the number of unique participants.

We have rectified the Abstract (Page 2, Line 64) and Introduction (Page 3, Line 138):

“We charted the organisational variability of structural (610 participants, N = 390 with one observation, N = 163 with two observations, and N = 57 with three) and functional (512 participants, N = 340 with one observation, N = 128 with two observations, and N = 44 with three)”.

The term “structural gradients” is ambiguous in the introduction. Clarify that these gradients were computed from structural and functional connectivity matrices, not from other structural features (e.g. cortical thickness).

We have clarified this in the Introduction (Page 3, Line 134):

“Applying diffusion-map embedding as an unsupervised machine-learning technique onto matrices of communicability (from streamline SIFT2-weighted fibre bundle capacity) and functional connectivity, we derived gradients of structural and functional brain organisation in children and adolescents…”

Page 5: The sentence, “we calculated the normalized angle of each structural and functional connectome to derive symmetric affinity matrices” is unclear and needs clarification.

We have clarified this within the second paragraph of the Results section (Page 4, Line 185):

“To capture inter-nodal similarity in connectivity, using a normalised angle kernel, we derived individual symmetric affinity matrices from the left and right hemispheres of each communicability and functional connectivity matrix. Varying kernels capture different but highly-related aspects of inter-nodal similarity, such as correlation coefficients, Gaussian kernels, and cosine similarity. Diffusion-map embedding is then applied on the affinity matrices to derive gradients of cortical organisation”. 

Figure 1.a: “Affine A” likely refers to the affinity matrix. The term “affine” may be confusing; consider using a clearer label. It would also help to add descriptive labels for rows and columns (e.g. region x region).

Thank you for this suggestion! We have replaced each of the labels with “pairwise similarity”. We also labelled the rows and columns as regions.

Figure 1.d: Are the cross-group differences statistically significant? If so, please indicate this in the figure.

We have added the results of a series of linear mixed effects models to the legend of Figure 1 (Page 6, line 252):

“indicates a significant effect of dataset (p < 0.05) on variance explained within a linear mixed effects model controlling for head motion, sex, and age at scan”.

The sentence “whose connectomes were successfully thresholded” in the methods is unclear. What does “successfully thresholded” mean? Additionally, this seems to be the first mention of the Schaefer 100 and Brainnetome atlas; clarify where these parcellations are used. 

We have amended the Methodology section (Page 23, Line 1138):

“For each participant, we retained the strongest 10% of connections per row, thus creating fully connected networks required for building affinity matrices. We excluded any connectomes in which such thresholding was not possible due to insufficient non-zero row values. To further ensure accuracy in connectome reconstruction, we excluded any participants whose connectomes failed thresholding in two alternative parcellations: the 100node Schaefer 7-network (Schaefer et al., 2018) and Brainnetome 246-node (Fan et al., 2016) parcellations, respectively”. 

We have also specified the use of the Schaefer 200-node parcellation in the first sentence on the second Results paragraph.

The use of “streamline counts” is misleading, as the method uses SIFT2-weighted fibre bundle capacity rather than raw streamline counts. It would be better to refer to this measure as “SIFT2-weighted fibre bundle capacity” or “FBC”.

We replaced all instances of “streamline counts” with “SIFT2-weighted fibre bundle capacity” as appropriate.

Figure 2.c: Consider adding plots showing changes in eccentricity against (1) degree centrality, and (2) weighted local clustering coefficient. Additionally, a plot showing the relationship between age and mean eccentricity (averaged across nodes) at the individual level would be informative.

We added the correlation between eccentricity and both degree centrality and the weighted local clustering coefficient and included them in our dominance analysis in Figure 2. In terms of the relationship between age and mean (global) eccentricity, these are plotted in Figure 3. 

Figure 2.b: Considering the results of the following sections, it would be interesting to include additional KDE/violin plots to show group differences in the distribution of eccentricity within 7 different functional networks.

As part of our analysis to parse neurotypicality and dataset effects, we tested for group differences in the distribution of structural and functional manifold eccentricity within each of the 7 functional networks in the referred and control portions of CALM and have included instances of significant differences with a coloured arrow to represent the direction of the difference within Figure 3. 

Figure 3: Several panels lack axis labels for x and y axes. Adding these would improve clarity.

To minimise the amount of text in Figure 3, we opted to include labels only for the global-level structural and functional results. However, to aid interpretation, we added a small schematic at the bottom of Figure 3 to represent all axis labels. 

The statement that “differences between datasets only emerged when taking development into account” seems inaccurate. Differences in eccentricity are evident across datasets even before accounting for development (see Fig 2.b and the significance in the Scheirer-Ray-Hare test).

We agree – differences in eccentricity across development and datasets are evident in structural and functional manifold eccentricity, as well as within structure-function coupling. However, effects of neurotypicality were particularly strong for the maturation of structure-function coupling, rather than magnitude. Therefore, we have rephrased this sentence in the Discussion (page 18, line 832):

“Furthermore, group-level structural and functional gradients were highly consistent across datasets, whilst differences between datasets were emphasised when taking development into account, through differing rates of structural and functional manifold expansion, respectively, alongside maturation of structure-function coupling”.

The handling of longitudinal data by adding a random effect for individuals is not clear in the main text. Mentioning this earlier could be helpful. 

We have included this detail in the second sentence of the “developmental trajectories of structural manifold contraction and functional manifold expansion” results sub-section (page 11, line 503):

“We included a random effect for each participant to account for longitudinal data”. 

Figure 4.b: Why were ranks shown instead of actual coefficient of variation values? Consider including a cortical map visualization of the coefficients in the supplementary material.

We visualised the ranks, instead of the actual coefficient of variation (CV) values, due to considerable variability and skew in the magnitude of the CV, ranging from 28.54 (in the right visual network) to 12865.68 (in the parietal portion of the left default-mode network), with a mean of 306.15. If we had visualised the raw CV values, these larger values would’ve been over-represented. We’ve also noticed and rectified an error in the labelling of the colour bar for Figure 4b: the minimum should be most variable (i.e. a rank of 1). To aid contextualisation of the ranks, we have added the following to the Results (page 14, line 626):

“The distribution of cortical coefficients of variation (CV) varied considerably, with the largest CV (in the parietal division of the left default-mode network) being over 400 times that of the smallest (in the right visual network). The distribution of absolute CVs was positively skewed, with a Fisher skewness coefficient g₁ of 7.172, meaning relatively few regions had particularly high inter-individual variability, and highly peaked, with a kurtosis of 54.883, where a normal distribution has a skewness coefficient of 0 and a kurtosis of 3”. 

Reviewer #2 (Public review):

Some differences in developmental trajectories between CALM and NKI (e.g. Figure 4d) are not explained. Are these differences expected, or do they suggest underlying factors that require further investigation?

This is a great point, and we appreciate the push to give a fuller explanation. It is very hard to know whether these effects are expected or not. We certainly don’t know of any other papers that have taken this approach. In response to the reviewer’s point, we decided to run some more analyses to better understand the differences. Having observed stronger age effects on structure-function coupling within the neurotypical NKI dataset, compared to the absent effects in the neurodivergent portion of CALM, we wanted to follow up and test that it really is that coupling is more sensitive to the neurodivergent versus neurotypical difference between CALM and NKI (rather than say, scanner or site effects). In short, we find stronger developmental effects of coupling within the neurotypical portion of CALM, rather than neurodivergent, and have added this to the Results (page 15, line 701):

“To further examine whether a closer correspondence of structure-function coupling with age is associated with neurotypicality, we conducted a follow-up analysis using the additional age-matched neurotypical portion of CALM (N = 77). Given the widespread developmental effects on coupling within the neurotypical NKI sample, compared to the absent effects in the neurodivergent portion of CALM, we would expect strong relationships between age and structure-function coupling with the neurotypical portion of CALM. This is indeed what we found: structure-function coupling showed a linear negative relationship with age globally (F = 16.76, p_FDR < 0.001, adjusted R² = 26.44%), alongside fronto-parietal (F = 9.24, p_FDR = 0.004, adjusted R² = 19.24%), dorsalattention (F = 13.162, p_FDR = 0.001, adjusted R²= 18.14%), ventral attention (F = 11.47, p_FDR  = 0.002, adjusted R²= 22.78), somato-motor (F = 17.37, p_FDR  < 0.001, adjusted R²= 21.92%) and visual (F = 11.79, p_FDR  = 0.002, adjusted R²= 20.81%) networks. Together, this supports our hypothesis that within neurotypical children and adolescents, structure-function coupling decreases with age, showing a stronger effect compared to their neurodivergent counterparts, in tandem with the emergence of higher-order cognition. Thus, whilst the magnitude of structure-function coupling across development appeared insensitive to neurotypicality, its maturation is sensitive. Tentatively, this suggests that neurotypicality is linked to stronger and more consistent maturational development of structure-function coupling, whereby the tethering of functional connectivity to structure across development is adaptive”. 

In conjunction with the Reviewer’s later request to deepen the Discussion, we have included an additional paragraph attempting to explain the differences in neurodevelopmental trajectories of structure-function coupling (Page 19, Line 924):

“Whilst the spatial patterning of structure-function coupling across the cortex has been extensively documented, as explained above, less is known about developmental trajectories of structure-function coupling, or how such trajectories may be altered in those with neurodevelopmental conditions. To our knowledge, only one prior study has examined differences in developmental trajectories of (non-manifold) structure-function coupling in typically-developing children and those with attention-deficit hyperactivity disorder (Soman et al., 2023), one of the most common conditions in the neurodivergent portion of CALM. Namely, using cross-sectional and longitudinal data from children aged between 9 and 14 years old, they demonstrated increased coupling across development in higher-order regions overlapping with the defaultmode, salience, and dorsal attention networks, in children with ADHD, with no significant developmental change in controls, thus encompassing an ectopic developmental trajectory (Di Martino et al., 2014; Soman et al., 2023). Whilst the current work does not focus on any condition, rather the broad mixed population of young people with neurodevelopmental symptoms (including those with and without diagnoses), there are meaningful individual and developmental differences in structure-coupling. Crucially, it is not the case that simply having stronger coupling is desirable. The current work reveals that there are important developmental trajectories in structure-function coupling, suggesting that it undergoes considerable refinement with age. Note that whilst the magnitude of structure-function coupling across development did not differ significantly as a function of neurodivergence, its relationship to age did. Our working hypothesis is that structural connections allow for the ordered integration of functional areas, and the gradual functional modularisation of the developing brain. For instance, those with higher cognitive ability show a stronger refinement of structurefunction coupling across development. Future work in this space needs to better understand not just how structural or functional organisation change with time, but rather how one supports the other”. 

The use of COMBAT may have excluded extreme participants from both datasets, which could explain the lack of correlations found with psychopathology.

COMBAT does not exclude participants from datasets but simply adjusts connectivity estimates. So, the use of COMBAT will not be impacting the links with psychopathology by removing participants. But this did get us thinking. Excluding participants based on high motion may have systematically removed those with high psychopathology scores, meaning incomplete coverage. In other words, we may be under-representing those at the more extreme end of the range, simply because their head-motion levels are higher and thus are more likely to be excluded. We found that despite certain high-motion participants being removed, we still had good coverage of those with high scores and were therefore sensitive within this range. We have added the following to the revised Methods section (Page 26, Line 1338):

“As we removed participants with high motion, this may have overlapped with those with higher psychopathology scores, and thus incomplete coverage. To examine coverage and sensitivity to broad-range psychopathology following quality control, we calculated the Fisher-Pearson skewness statistic g₁ for each of the 6 Conners t-statistic measures and the proportion of youth with a t-statistic equal to or greater than 65, indicating an elevated or very elevated score. Measures of inattention (g₁ = 0.11, 44.20% elevated), hyperactivity/impulsivity (g₁ = 0.48, 36.41% elevated), learning problems (g₁ = 0.45, 37.36% elevated), executive functioning (g₁ = 0.27, 38.16% elevated), aggression (g₁ = 1.65, 15.58% elevated), and peer relations (g₁ = 0.49, 38% elevated) were positively skewed and comprised of at least 15% of children with elevated or very elevated scores, suggesting sufficient coverage of those with extreme scores”. 

There is no discussion of whether the stable patterns of brain organization could result from preprocessing choices or summarizing data to the mean. This should be addressed to rule out methodological artifacts. 

This is a brilliant point. We are necessarily using a very lengthy pipeline, with many design choices to explore structural and functional gradients and their intersection. In conjunction with the Reviewer’s later suggestion to deepen the Discussion, we have added the following paragraph which details the sensitivity analyses we carried out to confirm the observed stable patterns of brain organization (Page 18, Line 863):

“That is, whilst we observed developmental refinement of gradients, in terms of manifold eccentricity, standard deviation, and variance explained, we did not observe replacement. Note, as opposed to calculating gradients based on group data, such as a sliding window approach, which may artificially smooth developmental trends and summarise them to the mean, we used participant-level data throughout. Given the growing application of gradient-based analyses in modelling structural (He et al., 2025; Li et al., 2024) and functional (Dong et al., 2021; Xia et al., 2022) brain development, we hope to provide a blueprint of factors which may affect developmental conclusions drawn from gradient-based frameworks”.

Although imputing missing data was necessary, it would be useful to compare results without imputed data to assess the impact of imputation on findings. 

It is very hard to know the impact of imputation without simply removing those participants with some imputed data. Using a simulation experiment, we expressed the imputation accuracy as the root mean squared error normalized by the range of observable data in each scale. This produced a percentage error margin. We demonstrate that imputation accuracy across all measures is at worst within approximately 11% of the observed data, and at best within approximately 4% of the observed data, and have included the following in the revised Methods section (Page 27, Line 1348):

“Missing data

To avoid a loss of statistical power, we imputed missing data. 27.50% of the sample had one or more missing psychopathology or cognitive measures (equal to 7% of all values), and the data was not missing at random: using a Welch’s t-test, we observed a significant effect of missingness on age [t (264.479) = 3.029, p = 0.003, Cohen’s d = 0.296], whereby children with missing data (M = 12.055 years, SD = 3.272) were younger than those with complete data (M = 12.902 years, SD = 2.685). Using a subset with complete data (N = 456), we randomly sampled 10% of the values in each column with replacement and assigned those as missing, thereby mimicking the proportion of missingness in the entire dataset. We conducted KNN imputation (uniform weights) on the subset with complete data and calculated the imputation accuracy as the root mean squared error normalized by the observed range of each measure. Thus, each measure was assigned a percentage which described the imputation margin of error. Across cognitive measures, imputation was within a 5.40% mean margin of error, with the lowest imputation error in the Trail motor speed task (4.43%) and highest in the Trails number-letter switching task (7.19%). Across psychopathology measures, imputation exhibited a mean 7.81% error margin, with the lowest imputation error in the Conners executive function scale (5.75%) and the highest in the Conners peer relations scale (11.04%). Together, this suggests that imputation was accurate”.

The results section is extensive, with many reports, while the discussion is relatively short and lacks indepth analysis of the findings. Moving some results into the discussion could help balance the sections and provide a deeper interpretation. 

We agree with the Reviewer and appreciate the nudge to expand the Discussion section. We have added 4 sections to the Discussion. The first explores the importance of the default-mode network as a region whose coupling is most consistently predicted by working memory across development and phenotypes, in terms of its underlying anatomy (Paquola et al., 2025) (Page 20, Line 977):

“An emerging theme from our work is the importance of the default-mode network as a region in which structure-function coupling is reliably predicted by working memory across neurodevelopmental phenotypes and datasets during childhood and adolescence. Recent neurotypical adult investigations combining highresolution post-mortem histology, in vivo neuroimaging, and graph-theory analyses have revealed how the underlying neuroanatomy of the default-mode network may support diverse functions (Paquola et al., 2025), and thus exhibit lower structure-function coupling compared to unimodal regions. The default-mode network has distinct neuroanatomy compared to the remaining 6 intrinsic resting-state functional networks (Yeo et al., 2011), containing a distinctive combination of 5 of the 6 von Economo and Koskinas cell types (von Economo & Koskinas, 1925), with an over-representation of heteromodal cortex, and uniquely balancing output across all cortical types. A primary cytoarchitectural axis emerges, beyond which are mosaic-like spatial topographies. The duality of the default-mode network, in terms of its ability to both integrate and be insulated from sensory information, is facilitated by two microarchitecturally distinct subunits anchored at either end of the cytoarchitectural axis (Paquola et al., 2025). Whilst beyond the scope of the current work, structure-function coupling and their predictive value for cognition may also differ across divisions within the default-mode network, particularly given variability in the smoothness and compressibility of cytoarchitectural landscapes across subregions (Paquola et al., 2025)”. 

The second provides a deeper interpretation and contextualisation of greater sensitivity of communicability, rather than functional connectivity, to neurodivergence (Page 19, Lines 907):

“We consider two possible factors to explain the greater sensitivity of neurodivergence to gradients of communicability, rather than functional connectivity. First, functional connectivity is likely more sensitive to head motion than structural-based communicability and suffers from reduced statistical power due to stricter head motion thresholds, alongside greater inter-individual variability. Second, whilst prior work contrasting functional connectivity gradients from neurotypical adults with those with confirmed ASD diagnoses demonstrated vertex-level reductions in the default-mode network in ASD and marginal increases in sensorymotor communities (Hong et al., 2019), indicating a sensitivity of functional connectivity to neurodivergence, important differences remain. Specifically, whilst the vertex-level group-level differences were modest, in line with our work, greater differences emerged when considering step-wise functional connectivity (SFC); in other words, when considering the dynamic transitions of or information flow through the functional hierarchy underlying the static functional connectomes, such that ASD was characterised by initial faster SFC within the unimodal cortices followed by a lack of convergence within the default-mode network (Hong et al., 2019). This emphasis on information flow and dynamic underlying states may point towards greater sensitivity of neurodivergence to structural communicability – a measure directly capturing information flow – than static functional connectivity”. 

The third paragraph situates our work within a broader landscape of reliable brain-behaviour relationships, focusing on the strengths of combining clinical and normative samples to refine our interpretation of the relationship between gradients and cognition, as well as the importance of equifinality in developmental predictive work (Page 20, line 994):

“In an effort to establish more reliable brain-behaviour relationships despite not having the statistical power afforded by large-scale, typically normative, consortia (Rosenberg & Finn, 2022), we demonstrated the development-dependent link between default-mode structure-function coupling and working memory generalised across clinical (CALM) and normative (NKI) samples, across varying MRI acquisition parameters, and harnessing within- and across-participant variation. Such multivariate associations are likely more reliable than their univariate counterparts (Marek et al., 2022), but can be further optimised using task-related fMRI (Rosenberg & Finn, 2022). The consistency, or lack of, of developmental effects across datasets emphasises the importance of validating brain-behaviour relationships in highly diverse samples. Particularly evident in the case of structure-function coupling development, through our use of contrasting samples, is equifinality (Cicchetti & Rogosch, 1996), a key concept in developmental neuroscience: namely, similar ‘endpoints’ of structure-function coupling may be achieved through different initialisations dependent on working memory. 

The fourth paragraph details methodological limitations in response to Reviewer 1’s suggestions to justify the exclusion of subcortical regions and consider the role of spatial smoothing in structural connectome construction as well as the threshold for filtering short streamlines”. 

While the methods are thorough, it is not always clear whether the optimal approaches were chosen for each step, considering the available data. 

In response to Reviewer 1’s concerns, we conducted several sensitivity analyses to evaluate the robustness of our results in terms of procedure. Specifically, we evaluated the impact of thresholding (full or sparse), level of analysis (individual or group gradients), construction of the structural connectome (communicability or fibre bundle capacity), Procrustes rotation (alignment to group-level gradients before Procrustes), tracking the variance explained in individual connectomes by group-level gradients, impact of head motion, and distinguishing between site and neurotypicality effects. All these analyses converged on the same conclusion: whilst we observe some developmental refinement in gradients, we do not observe replacement. We refer the reviewer to their third point, about whether stable patterns of brain organization were artefactual. 

The introduction is overly long and includes numerous examples that can distract readers unfamiliar with the topic from the main research questions. 

We have removed the following from the Introduction, reducing it to just under 900 words:

“At a molecular level, early developmental patterning of the cortex arises through interacting gradients of morphogens and transcription factors (see Cadwell et al., 2019). The resultant areal and progenitor specialisation produces a diverse pool of neurones, glia, and astrocytes (Hawrylycz et al., 2015). Across childhood, an initial burst in neuronal proliferation is met with later protracted synaptic pruning (Bethlehem et al., 2022), the dynamics of which are governed by an interplay between experience-dependent synaptic plasticity and genomic control (Gottlieb, 2007)”.

“The trends described above reflect group-level developmental trends, but how do we capture these broad anatomical and functional organisational principles at the level of an individual?”

We’ve also trimmed the second Introduction paragraph so that it includes fewer examples, such as removal of the wiring-cost optimisation that underlies structural brain development, as well as removing specific instances of network segregation and integration that occur throughout childhood.

Author response:

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

Reviewer #1 (Public Review): 

Strengths: 

The work uses a simple and straightforward approach to address the question at hand: is dynein a processive motor in cells? Using a combination of TIRF and spinning disc confocal microscopy, the authors provide a clear and unambiguous answer to this question. 

Thank you for the recognition of the strength of our work

Weaknesses: 

My only significant concern (which is quite minor) is that the authors focus their analysis on dynein movement in cells treated with docetaxol, which could potentially affect the observed behavior. However, this is likely necessary, as without it, motility would not have been observed due to the 'messiness' of dynein localization in a typical cell (e.g., plus end-tracking in addition to cargo transport).

You are exactly correct that this treatment was required to provided us a clear view of motile dynein and p50 puncta. One concern about the treatment that we had noted in our original submission was that the docetaxel derivative SiR tubulin could increase microtubule detyrosination, which has been implicated in affecting the initiation of dynein-dynactin motility but not motility rates (doi: 10.15252/embj.201593071). In response to a comment from reviewer 2 we investigated whether there was a significant increase in alpha-tubulin detyrosination in our treatment conditions and found that there was not. We have removed the discussion of this possibility from the revised version. Please also see response to comments raised by reviewer 2. 

Reviewer 1 (Recommendations for the authors):

Major points: 

(1) The authors measured kinesin-1-GFP intensities in a different cell line (drosophila S2 cells) than what was used for the DHC and p50 measurements (HeLa cells). It is unclear if this provides a fair comparison given the cells provide different environments for the GFP. Although the differences may in fact be trivial, without somehow showing this is indeed a fair comparison, it should at least be noted as a caveat when interpreting relative intensity differences. Alternatively, the authors could compare DHC and p50 intensities to those measured from HeLa cells treated with taxol. 

Thank you for this suggestion. We conducted new rounds of imaging with the DHCEGFP and p50-EGFP clones in conjunction with HeLa cells transiently expressing the human kinesin-1-EGFP and now present the datasets from the new experiments. Importantly, our new data was entirely consistent with the prior analyses as there was not a significant difference between the kinesin-1-EGFP dimer intensities and the DHC-EGFP puncta intensities and there was a statistically significant difference in the intensity of p50 puncta, which were approximately half the intensity of the kinesin-1 and DHC. We have moved the old data comparing the intensities in S2 cells expressing kinesin-1-EGFP to Figure 3 - figure supplement 2 A-D and the new HeLa cell data is now shown in Figure 3 D-G.

(2) Given the low number of observations (41-100 puncta), I think a scatter plot showing all data points would offer readers a more transparent means of viewing the single-molecule data presented in Figures 3A, B, C, and G. I also didn't see 'n' values for plots shown in Figure 3. 

The box and whisker plots have now been replaced with scatter plots showing all data points. The accompanying ‘n’ values have been included in the figure 3 legend as well as the histograms in figures 1 and 2 that are represented in the comparative scatter plots.  

(3) Given the authors have produced a body of work that challenges conclusions from another pre-print (Tirumala et al., 2022 bioRxiv) - specifically, that dynein is not processive in cells - I think it would be useful to include a short discussion about how their work challenges theirs. For example, one significant difference between the two experimental systems that may account for the different observations could simply be that the authors of the Tirumala study used a mouse DHC (in HeLa cells), which may not have the ability to assemble into active and processive dynein-dynactin-adaptor complexes. 

Thank you for pointing this out! At the time we submitted our manuscript we were conflicted about citing a pre-print that had not been peer reviewed simply to point out the discrepancy. If we had done so at that time we would have proposed the exact potential technical issue that you have proposed here. However, at the time we felt it would be better for these issues to be addressed through the review process. Needless to say, we agree with your interpretation and now that the work is published (Tirumala et al. JCB, 2024) it is entirely appropriate to add a discussion on Tirumala et al. where contradictory observations were reported. 

The following statement has been added to the manuscript: 

“In contrast, a separate study (Tirumala et al., 2024) reported that dynein is not highly processive, typically exhibiting runs of very short duration (~0.6 s) in HeLa cells. A notable technical difference that may account for this discrepancy is that our study visualizes endogenously tagged human DHC, whereas Tirumala et al. characterized over-expressed mouse DHC in HeLa cells. Over-expression of the DHC may result in an imbalance of the subunits that comprise the active motor complex, leading to inactive, or less active complexes. Similarly, mouse DHC may not have the ability to efficiently assemble into active and processive dynein-dynactin-adaptor complexes to the same extent as human DHC.”

Minor points: 

(1) "Specifically, the adaptor BICD2 recruited a single dynein to dynactin while BICDR1 and HOOK3 supported assembly of a "double dynein" complex." It would be more accurate to say that dynein-dynactin complexes assembled with Bicd2 "tend to favor single dynein, and the Bicdr1 and Hook3 tend to favor two dyneins" since even Bicd2 can support assembly of 2 dynein-1 dynactin complexes (see Urnavicius et al, Nature 2018). 

Thank you, the manuscript has been edited to reflect this point. 

(2) "Human HeLa cells were engineered using CRISPR/Cas9 to insert a cassette encoding FKBP and EGFP tags in the frame at the 3' end of the dynein heavy chain (DYNC1H1) gene (SF1)." It is unclear to what "SF1" is referring. 

SF1 is supplementary figure 1, which we have now clarified as being Figure 1 – figure supplement 1A.

(3) "The SiR-Tubulin-treated cells were subjected to two-color TIRFM to determine if the DHC puncta exhibited motility and; indeed, puncta were observed streaming along MTs..." This sentence is strangely punctuated (the ";" is likely a typo?). 

Thank you for pointing this out, the typo has been corrected and the sentence now reads:

“The SiR-Tubulin-treated cells were subjected to two-color TIRFM and DHC-EGFP puncta were clearly observed streaming on Sir-Tubulin labeled MTs, which was especially evident on MTs that were pinned between the nucleus and the plasma membrane (Video 3)”

(4) I am unfamiliar with the "MK" acronym shown above the molecular weight ladders in Figure 3H and I. Did the authors mean to use "MW" for molecular weight? 

We intended this to mean MW and the typo has been corrected.

(5) "This suggests that the cargos, which we presume motile dynein-dynactin puncta are bound to, any kinesins..." This sentence is confusing as written. Did the authors mean "and kinesins"? 

Agreed. We have changed this sentence to now read: 

“The velocity and low switching frequency of motile puncta suggest that any kinesin motors associated with cargos being transported by the dynein-dynactin visualized here are inactive and/or cannot effectively bind the MT lattice during dynein-dynactin-mediated transport in interphase HeLa cells.”

Reviewer 2 (Recommendations for the authors):

(1) I am confused as to why the authors introduced an FKBP tag to the DHC and no explanation is given. Is it possible this tag induces artificial dimerization of the DHC? 

FKBP was tagged to DHC for potential knock sideways experiments. Since the current cell line does not express the FKBP counterpart FRB, having FKBP alone in the cell line would not lead to artificial dimerization of DHC.

(2) The authors use a high concentration of SiR-tubulin (1uM) before washing it out. However, they observe strong effects on MT dynamics. The manufacturer states that concentrations below 100nM don't affect MT dynamics, so I am wondering why the authors are using such a high amount that leads to cellular phenotypes. 

We would like to note that in our hands even 100 nM SiR-tubulin impacted MT dynamics if it was incubated for enough time to get a bright signal for imaging, which makes sense since drugs like docetaxel and taxol become enriched in cells over time. Thus, it was a trade-off between the extent/brightness of labeling and the effects on MT dynamics. We opted for shorter incubation with a higher concentration of Sir-Tubulin to achieve rapid MT labeling and efficient suppression of plus-end MT polymerization. This approach proved useful for our needs since the loss of the tip-tacking pool of DHC provided a clearer view of the motile population of MT-associated DHC.

(3) The individual channels should be labeled in the supplemental movies. 

They have now been labelled.

(4) I would like to see example images and kymographs of the GFP-Kinesin-1 control used for fluorescent intensity analysis. Further, the authors use the mean of the intensity distribution, but I wonder why they don't fit the distribution to a Gaussian instead, as that seems more common in the field to me. Do the data fit well to a Gaussian distribution? 

Example images and kymographs of the kinesin-1-EGFP control HeLa cells used for the updated fluorescent intensity analysis have been now added to the manuscript in Figure 3 - figure supplement 1. The kinesin-1-EGFP transiently expressed in HeLa cells exhibited a slower mean velocity and run length than the endogenously tagged HeLa dynein-dynactin. Regarding the distribution, we applied 6 normality tests to the new datasets acquired with DHC and p50 in comparison to human kinesin-EGFP in HeLa cells. While we are confident concluding that the data for p50 was normally distributed (p > 0.05 in 6/6), it was more difficult to reach conclusions about the normality of the datasets for kinesin-1 (p > 0.05 in 4/6) and DHC (p > 0.5 in 1/6). We have decided to report the data as scatter plots (per the suggestion in major point 1 by reviewer 1) in the new Figure 3G since it could be misleading to fit a non-normal distribution with a single Gaussian. We note that the likely non-normal distribution of the DHC data (since it “passed” only 1/6 normality tests) could reflect the presence of other populations (e.g. 1 DHC-EGFP in a motile puncta), but we could also not confidently conclude this since attempting to fit the data with a double Gaussian did not pass statistical muster. Indeed, as stated in the text, on lines 197-198 we do not exclude that the range of DHC intensities measured here may include sub-populations of complexes containing a single dynein dimer with one DHC-EGFP molecule.   

Ultimately, we feel the safest conclusion is that there was not a statically significant difference between the DHC and kinesin-1 dimers (p = 0.32) but there was a statistically significant difference between both the DHC and kinesin-1 dimers compared to the p50 (p values < 0.001), which was ~50% the intensity of DHC and kinesin-1. Altogether this leads us to the fairly conservative conclusion that DHC puncta contain at least one dimer while the p50 puncta likely contain a single p50-EGFP molecule. 

(5) The authors suggest the microtubules in the cells treated with SiR-tubulin may be more detyrosinated due to the treatment. Why don't they measure this using well-characterized antibodies that distinguish tyrosinated/detyrosinated microtubules in cells treated or not with SiR-tubulin? 

At your suggestion, we carried out the experiment and found that under our labeling conditions there was not a notable difference in microtubule detyrosination between DMSO- and SiR-Tubulin-treated cells. Thus, we have removed this caveat from the revised manuscript.

(6) "While we were unable to assess the relative expression levels of tagged versus untagged DHC for technical reasons." Please describe the technical reasons for the inability to measure DHC expression levels for the reader.

We made several attempts to quantify the relative amounts of untagged and tagged protein by Western blotting. The high molecular weight of DHC (~500kDa) makes it difficult to resolve it on a conventional mini gel. We attempted running a gradient mini gel (4%-15%), and doing a western blot; however, we were still unable to detect DHC. To troubleshoot, the experiments were repeated with different dilutions of a commercially available antibody and varying concentrations of cell lysate; however, we were unable to obtain a satisfactory result. 

We hold the view that even if it had it worked it would have been difficult to detect a relatively small difference between the untagged (MW = 500kDa) and tagged DHC (MW = 527kDa) by western blot. We have added language to this effect in the revised manuscript. 

Reviewer #3 (Public Review):

(1). CRISPR-edited HeLa clones: 

(i) The authors indicate that both the DHC-EGFP and p50-EGFP lines are heterozygous and that the level of DHC-EGFP was not measured due to technical difficulties. However, quantification of the relative amounts of untagged and tagged DHC needs to be performed - either using Western blot, immunofluorescence or qPCR comparing the parent cell line and the cell lines used in this work. 

See response to reviewer 2 above. 

(ii) The localization of DHC predominantly at the plus tips (Fig. 1A) is at odds with other work where endogenous or close-to-endogenous levels of DHC were visualized in HeLa cells and other non-polarized cells like HEK293, A-431 and U-251MG (e.g.: OpenCell (https://opencell.czbiohub.org/target/CID001880), Human Protein Atlas  ), https://www.biorxiv.org/content/10.1101/2021.04.05.438428v3). The authors should perform immunofluorescence of DHC in the parental cells and DHC-EGFP cells to confirm there are no expression artifacts in the latter. Additionally, a comparison of the colocalization of DHC with EB1 in the parental and DHC-EGFP and p50-EGFP lines would be good to confirm MT plus-tip localisation of DHC in both lines. 

The microtubule (MT) plus-tip localization of DHC was already observed in the 1990s, as evidenced by publications such as (PMID:10212138) and (PMID:12119357), which were further confirmed by Kobayashi and Murayama  in 2009 (PMID:19915671). We hold the view that further investigation into this localization is not worthwhile since the tip-tracking behavior of DHC-dynactin has been long-established in the field.

(iii) It would also be useful to see entire fields of view of cells expressing DHC-EGFP and p50EGFP (e.g. in Spinning Disk microscopy) to understand if there is heterogeneity in expression. Similarly, it would be useful to report the relative levels of expression of EGFP (by measuring the total intensity of EGFP fluorescence per cell) in those cells employed for the analysis in the manuscript. 

Representative images of fields have been added as Figure 1 - figure supplement 1B and Figure 2 – figure supplement 1 in the revised manuscript. We did not see drastic cell-tocell variation of expression within the clonal cell lines.

(iv) Given that the authors suspect there is differential gene regulation in their CRISPR-edited lines, it cannot be concluded that the DHC-EGFP and p50-EGFP punctae tracked are functional and not piggybacking on untagged proteins. The authors could use the FKBP part of the FKBPEGFP tag to perform knock-sideways of the DHC and p50 to the plasma membrane and confirm abrogation of dynein activity by visualizing known dynein targets such as the Golgi (Golgi should disperse following recruitment of EGFP-tagged DHC-EGFP or p50-EGFP to the PM), or EGF (movement towards the cell center should cease). 

Despite trying different concentrations and extensive troubleshooting, we were not able to replicate the reported observations of Ciliobrevin D or Dynarrestin during mitosis. We would like to emphasize that the velocity (1.2 μm/s) of dynein-dynactin complexes that we measured in HeLa cells was comparable to those measured in iNeurons by Fellows et al. (PMID: 38407313) and for unopposed dynein under in vitro conditions. 

(2) TIFRM and analysis: 

(i) What was the rationale for using TIRFM given its limitation of visualization at/near the plasma membrane? Are the authors confident they are in TIRF mode and not HILO, which would fit with the representative images shown in the manuscript? 

To avoid overcrowding, it was important to image the MT tracks that that were pinned between the nucleus and the plasma membrane. It is unclear to us why the reviewer feels that true TIRFM could not be used to visualize the movement of dynein-dynactin on this population of MTs since the plasma membrane is ~ 3-5 nm and a MT is ~25-27 nm all of which would fall well within the 100-200 nm excitable range of the evanescent wave produced by TIRF. While we feel TIRF can effectively visualize dynein-dynactin motility in cells, we have mentioned the possibility that some imaging may be HILO microscopy in the materials and methods.

(ii) At what depth are the authors imaging DHC-EGFP and p50-EGFP? 

The imaging depth of traditional TIRFM is limited to around 100-200 nm. In adherent interphase HeLa cells the nucleus is in very close proximity (nanometer not micron scale) to the plasma membrane with some cytoskeletal filaments (actin) and microtubules positioned between the plasma membrane and the nuclear membrane. The fact that we were often visualizing MTs positioned between the nucleus and the membrane makes us confident that we were imaging at a depth (100 - 200nm) consistent with TIRFM. 

(iii) The authors rely on manual inspection of tracks before analyzing them in kymographs - this is not rigorous and is prone to bias. They should instead track the molecules using single particle tracking tools (eg. TrackMate/uTrack), and use these traces to then quantify the displacement, velocity, and run-time. 

Although automated single particle tracking tools offer several benefits, including reduced human effort, and scalability for large datasets, they often rely on specialized training datasets and do not generalize well to every dataset. The authors contend that under complex cellular environments human intervention is often necessary to achieve a reliable dataset. Considering the nature of our data we felt it was necessary to manually process the time-lapses. 

(iv) It is unclear how the tracks that were eventually used in the quantification were chosen. Are they representative of the kind of movements seen? Kymographs of dynein movement along an entire MT/cell needs to be shown and all punctae that appear on MTs need to be tracked, and their movement quantified. 

Considering the densely populated environment of a cell, it will be nearly impossible to quantity all the datasets. We selected tracks for quantification, focusing on areas where MTs were pinned between the nucleus and plasma membrane where we could track the movement of a single dynein molecule and where the surroundings were relatively less crowded. 

(v) What is the directionality of the moving punctae? 

In our experience, cells rarely organized their MTs in the textbook radial MT array meaning that one could not confidently conclude that “inward” movements were minus-end directed. Microtubule polarity was also not able to be determined for the MTs positioned between the plasma membrane and the nucleus on which many of the puncta we quantified were moving. It was clear that motile puncta moving on the same MT moved in the same direction with the exception of rare and brief directional switching events. What was more common than directional switching on the same MT were motile puncta exhibiting changes in direction at sharp (sometimes perpendicular) angles indicative of MT track switching, which is a well-characterized behavior of dynein-dynactin (See DOI: 10.1529/biophysj.107.120014).

(vi) Since all the quantification was performed on SiR tubulin-treated cells, it is unclear if the behavior of dynein observed here reflects the behavior of dynein in untreated cells. Analysis of untreated cells is required. 

It was important to quantify SiR tubulin-treated cells because SiR-Tubulin is a docetaxel derivative, and its addition suppressed plus-end MT polymerization resulting in a significant reduction in the DHC tip-tracking population and a clearer view of the motile population of MT-associated DHC puncta. Otherwise, it was challenging to reliably identify motile puncta given the abundance of DHC tip-tracking populations in untreated cells.  

(3) Estimation of stoichiometry of DHC and p50 

Given that the punctae of DHC-EGFP and p50 seemingly bleach on MT before the end of the movie, the authors should use photobleaching to estimate the number of molecules in their punctae, either by simple counting the number of bleaching steps or by measuring single-step sizes and estimating the number of molecules from the intensity of punctae in the first frame. 

Comparing the fluorescence intensity of a known molecule (in our case a kinesin-1EGFP dimer) to calculate the numbers of an unknown protein molecule (in our case Dynein or p50) is a widely accepted technique in the field. For example, refer to PMID: 29899040. To accurately estimate the stoichiometry of DHC and p50 and address the concerns raised by other reviewers, we expressed the human kinesin-EGFP in HeLa cells and analyzed the datasets from new experiments. We did not observe any significant differences between our old and new datasets.

(4) Discussion of prior literature 

Recent work visualizing the behavior of dyneins in HeLa cells (DOI:  10.1101/2021.04.05.438428), which shows results that do not align with observations in this manuscript, has not been discussed. These contradictory findings need to be discussed, and a more objective assessment of the literature in general needs to be undertaken.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

Overall, it's a well-performed study, however, causality between Plscr1 and Ifnlr1 expression needs to be more firmly established. This is because two recent studies of PLSCR1 KO cells infected with different viruses found no major differences in gene expression levels compared with their WT controls (Xu et al. Nature, 2023; LePen et al. PLoS Biol, 2024). There were also defects in the expression of other cytokines (type I and II IFNs plus TNF-alpha) so a clear explanation of why Ifnlr1 was chosen should also be given.

We appreciate the reviewer’s reference to the two recently published research on PLSCR1’s role in SARS-CoV-2 infections. We have also discussed those studies in the Introduction and Discussion sections of this manuscript. Here, we would like to clarify ourselves for the rationale of investigating Ifn-λr1 signaling.

The reviewer mentioned “defects in the expression of other cytokines (type I and II IFNs plus TNF-alpha)” and requested a clearer explanation of why Ifnlr1 was chosen for study. In our investigation of IAV infection, we observed no defects in the expression of type I and II IFNs or TNF-α in Plscr1^-/- mice; rather, these cytokines were expressed at even higher levels compared to WT controls (Figures 2D and 3A). This indicates that the type I and II IFN and TNF-α signaling pathways remain intact and are not negatively affected by the loss of Plscr1. Notably, Ifn-λr1 expression is the only one among all IFNs and their receptors that is significantly impaired in Plscr1^-/- mice (Figure 3A), justifying our focused investigation of this receptor. To further clarify this point, we have expanded the explanation under the section titled “Plscr1 Binds to Ifn-λr1 Promoter and Activates Ifn-λr1 Transcription in IAV Infection” within the Results. The reviewer noted that previously published studies “found no major differences in gene expression levels compared with their WT controls”, but neither study examined Ifn-λr1 expression.

(1) The authors propose that Plscr1 restricts IAV infection by regulating the type III IFN signaling pathway. While the data show a positive correlation between Ifnlr1 and Plscr1 levels in both mouse and cell culture models, additional evidence is needed to establish causality between the impaired type III IFN pathway, and the increased susceptibility observed in Plscr1-KO mice. To strengthen this conclusion, the following experiments could be undertaken: (i) Measure IAV titers in WT, Plscr1-KO, Ifnlr1-KO, and Plscr1/ Ifnlr1-double KO cells. If the antiviral activity of Plscr1 is highly dependent on Ifnlr1, there should be no further increase in IAV titers in double KO cells compared to single KO cells; (ii) over-express Plscr1 in Ifnlr1-KO cells to determine if it still inhibits IAV infection. If Plscr1's main action is to upregulate Ifnlr1, then it should not be able to rescue susceptibility since Ifnlr1 cannot be expressed in the KO background. If Plscr1 over-expression rescues viral susceptibility, then there are Ifnlr1-independent mechanisms involved. These experiments should help clarify the relative contribution of the type III IFN pathway to Plscr1-mediated antiviral immunity.

We agree with the reviewer that additional evidence is necessary to establish causality between the impaired type III IFN pathway and the increased susceptibility observed in Plscr1-KO mice. As requested by the reviewer, and one step further, we have measured IAV titers in Wt, Plscr1^-/-, Ifn-λr1^-/-, and Plscr1^-/-Ifn-λr1^-/- mouse lungs, which provided us with more comprehensive information at the tissue and organismal level compared to cell culture models. Our results are detailed under “The Anti-Influenza Activity of Plscr1 Is Highly Dependent on Ifn-λr1” within “Results” section and in Supplemental Figure 5. Importantly, there was no further increase in weight loss (Supplemental Figure 5B), total BAL cell counts (Supplemental Figure 5C), neutrophil percentages (Supplemental Figure 5D), and IAV titers (Supplemental Figure 5E) in Plscr1^-/-Ifn-λr1^-/- mouse lungs compared to Ifn-λr1^-/- mouse lungs. These findings indicate that the antiviral activity of Plscr1 is largely dependent on Ifn-λr1.

We agree that overexpression of Plscr1 on an Ifn-λr1^-/- background would provide additional evidence to support our conclusion from the Plscr1^-/-Ifn-λr1^-/- mice. In future studies, we plan to specifically overexpress Plscr1 in ciliated epithelial cells on the Ifn-λr1^-/- background by breeding Plscr1^floxStopFoxj1-Cre⁺Ifn-λr1^-/- mice. In addition, ciliated epithelial cells isolated from Ifn-λr1^-/- murine airways could be transduced with a Plscr1 construct for overexpression. We hypothesize that overexpression of Plscr1 in ciliated epithelial cells will not rescue susceptibility in Ifn-λr1^-/- mice or cells, since our Plscr1^-/-Ifn-λr1^-/- mouse model suggest that Ifn-λr1-independent anti-influenza functions of Plscr1 are likely minor compared to its role in upregulating Ifn-λr1. These future plans have been added to the “Discussion” section, and we look forward to presenting our results in a forthcoming publication.

(3) In Figure 4, the authors demonstrate the interaction between Plscr1 and Ifnlr1. They suggest that this interaction modulates IFN-λ signaling. However, Figures 5C-E show that the 5CA mutant, which lacks surface localization and the ability to bind Ifnlr1, exhibits similar anti-flu activity to WT Plscr1. Does this mean the interaction between Plscr1 and Ifnlr1 is dispensable for Plscr1-mediated antiviral function? Can the authors compare the activation of IFN-λ signaling pathway in Plscr1-KO cells expressing empty vector, WT Plscr1, and 5CA mutant? This could be done by measuring downstream ISG expression or using an ISRE-luciferase reporter assay upon IFN-λ treatment.

We agree with the reviewer that downstream activation of the IFN-λ signaling pathway is a critical component of the proposed regulatory role of PLSCR1. As suggested, we attempted to perform an ISRE-luciferase reporter assay following IFN-λ treatment in PLSCR1 rescue cell lines by transfecting the cells with hGAPDH-rLuc (Addgene #82479) and pGL4.45 [luc2P/ISRE/Hygro] (Promega #E4041).

Despite extensive efforts over several months, we were unable to achieve expression of pGL4.45 [luc2P/ISRE/Hygro] in PLSCR1 rescue cells using either Lipofectamine 3000 or electroporation, as no firefly luciferase activity was detected at baseline or following IFN-λ treatment. In contrast, hGAPDH-rLuc was robustly expressed in these cells.

The pGL4.45 [luc2P/ISRE/Hygro] plasmid was obtained directly from Promega as a purified product, and its sequence was confirmed via whole plasmid sequencing. Additionally, both hGAPDH-rLuc and pGL4.45 [luc2P/ISRE/Hygro] were successfully expressed in 293T cells, indicating that neither the plasmids nor the transfection protocols are inherently faulty.

We suspect that prior modifications to the PLSCR1 rescue cells—such as CRISPR-mediated knockout and lentiviral transduction—may interfere with successful transfection of pGL4.45 [luc2P/ISRE/Hygro] through an as-yet-unknown mechanism. Although these results are disappointing, we will continue troubleshooting and plan to communicate in a separate manuscript once the luciferase assay is successfully established.

Reviewer #1 (Recommendations):

(1) In the introduction, the linkage between the paragraph discussing type III IFN and PLSCR1 needs to be better established. The mention of PLSCR1 being an ISG at the outset may help connect these two paragraphs and make the text appear more logical.

We apologize for the lack of linkage and logic between type 3 IFN and PLSCR1. We have introduced PLSCR1 as an ISG at the beginning of its paragraph as recommended. 

(2) The statement that, “Intriguingly, PLSCR1 is also an antiviral ISG, as its expression can be highly induced by type 1 and 2 interferons in various viral infections[15, 16]. However, whether its expression can be similarly induced by type 3 interferon has not been studied yet.” is incorrect. Xu et al. tested the role of PLSCR1 in type III IFN-induced control of SARS-CoV-2 (ref. 24). This needs to be revised.

We apologize for the incorrect information in the introduction and have revised the paragraph with the proper citation.

(3) In Figure 3B, can the authors provide a comprehensive heatmap that includes all ISGs above the threshold, rather than only a subset? This would offer a more complete overview of the changes in type I, II, and III IFN pathways in Plscr1-KO mice.

As suggested by the reviewer, we have provided a comprehensive heatmap that includes all ISGs above the threshold in Figure 3C (previously Figure 3B). We identified a total of 1,113 ISGs in our dataset with a fold change ≥2. Enlarged heatmaps with gene names are provided in Supplemental Figure 1. Among those ISGs, 584 are regulated exclusively by type 1 IFNs, and 488 are regulated by both type 1 and type 2 interferons. Unfortunately, the Interferome database does not include information on type 3 IFN-inducible genes in mice[1]. Although many ISGs were robustly upregulated in Plscr1^-/- infected lungs, consistent with inflammation data, a large subset of ISGs failed to be transcribed when Ifn-λr1 function was impaired, especially at 7 dpi. We suspect that those non-transcribed ISGs in Plscr1^-/- mice may be specifically regulated by type 3 IFN and represent interesting targets for future research. These results have been added to “Plscr1 Binds to Ifn-λr1 Promoter and Activates Ifn-λr1 Transcription in IAV Infection” within “Results” section.

(4) In Figure 3C, 5B and 7H, immunoblots should also be included to measure changes of Ifnlr1/IFNLR1 protein level.

As requested by the reviewer, we have provided western blots measuring Ifn-λr1/IFN-λR1 protein level in Figure 5B and 7I. The protein expressions were consistent with the PCR results.

(5) In Figure 3H, the amount of RPL30 is also low in the anti-PLSCR1-treated and IgG samples, making it difficult to estimate if ChIP binding is genuinely impacted.

RPL30 Exon 3 serves as a negative control in the ChIP experiment and is not expected to bind either the anti-PLSCR1-treated or the IgG control samples. Anti-Histone H3 treatment is a positive control, with the treated sample expected to show binding to RPL30 Exon 3. We hope this clarification has addressed any further potential confusion from the reviewer.

(6) In Figure 4A, can the authors show a larger slice of the gel with molecular weight markers for both Plscr1 and Ifnlr1. In the coIP, the binding may be indirect through intermediate partners. Proximity ligation assay is a more direct assay for interaction and can be stated as such.

As suggested by the reviewer, we have included whole gel images of Figure 4A with molecular weight markers for both Plscr1 and Ifnlr1 in Supplemental Figure 3. We appreciate the reviewer’s affirmation of proximity ligation assay and have stated it as a more direct assay for interaction under “Plscr1 Interacts with Ifn-λr1 on Pulmonary Epithelial Cell Membrane in IAV Infection” in “Results” section.

(7) In Figure 5A, how is the expression of PLSCR1 WT and mutants driven by an EF-1α promoter can be further upregulated by IAV infection? Can the authors also use immunoblots to examine the protein level of PLSCR1?

We apologize for the confusion and appreciate the reviewer’s careful observation. We were initially surprised by this finding as well, but upon further investigation, we found out that the human PLSCR1 primers used in our qRT-PCR assay can still detect the transcription from the undisturbed portion of the endogenous PLSCR1 mRNA, even in PLSCR1^-/- cells. In the original Figure 5A, data for vector-transduced PLSCR1^-/- were not included because PCR was not performed on those samples at the time. After conducting PCR for vector-transduced PLSCR1^-/- cells, we detected transcription of PLSCR1, which confirms that the signaling originates from endogenous DNA, but not from the EF-1α promoter-driven PLSCR1 plasmid. Please see Author response image 1 below.

Author response image 1.

The forward human PLSCR1 primer we used matches 15-34 nt of Wt PLSCR1, and the reverse primer matches 224-244 nt of Wt PLSCR1. CRISPR-Cas9 KO of PLSCR1 was mediated by sgRNAs in A549 cells and was performed by Xu et al[2]. sgRNA #1 matches 227-246 nt, sgRNA #2 matches 209-228 nt, and sgRNA #3 matches 689-708 nt of Wt PLSCR1. The sgRNAs likely introduced a short deletion or insertion that does not affect transcription. However, those endogenous mRNA transcripts cannot be translated to functional and detectable PLSCR1 proteins, as validated by our western blot (below), as well as western blots performed by Xu et al[2]. Therefore, our primers could amplify endogenous PLSCR1 transcripts upregulated by IAV infection, if 15-244 nt was not disturbed by CRISPR-Cas9 KO. By western blot, we confirmed that only endogenous PLSCR1 expression is upregulated by IAV infection, and exogenous protein expression of PLSCR1 plasmids driven by an EF-1α promoter are not upregulated by IAV infection.

Author response image 2.

To avoid confusion, we have removed the original Figure 5A from the manuscript.

(8) In Figure 5C, the loss of anti-flu activity with the H262Y mutant is modest, suggesting the loss of ifnlr1 transcription is only partly responsible for the susceptibility of Plscr1 KO cells. The anti-flu activity being independent of scramblase activity resembles the earlier discovery of SARS-CoV-2 (Xu et al., 2024). This could be stated in the results since it is an important point that scramblase activity is dispensable for several major human viruses and shifts the emphasis regarding mechanism. It has been appropriately noted in the discussion.

We appreciated the comments and have acknowledged the consistency of our results with those of Xu et al. under “Both Cell Surface and Nuclear PLSCR1 Regulates IFN-λ Signaling and Limits IAV Infection Independent of Its Enzymatic Activity” in the “Results” section.

Reviewer #2 (Recommendations):

(1) The statement that type I interferons are expressed by “almost all cells” is inaccurate (line 61). Type I IFN production is also context-dependent and often restricted to specific cell types upon infection or stimulation.

We apologize for the inaccurate description of the expression pattern of type 1 IFNs and have corrected the restricted cellular sources of type 1 IFNs in the “Introduction”.

(2) The antiviral response is assessed solely through flu M gene expression. Incorporating infectious virus titers (e.g., TCID50 or plaque assay) would provide a more robust and direct measure of antiviral activity.

As requested by the reviewer, we have performed plaque assays on all experiments where flu M gene expression levels were measured (Figure 1G, 5E and 7F, and Supplemental Figure 6E). The plaque assay results are consistent with the flu M gene expressions.

(3) While mRNA expression of interferons is measured, protein levels (e.g., through ELISA) should also be quantified to establish the functional relevance of IFN expression changes.

As requested by the reviewer, we have quantified the protein level of IFN-λ in mouse BAL with ELISA (Figure 2E). The ELISA results are consistent with the mRNA expressions of IFN-λ.

(4) It is unclear whether reduced IFNLR1 expression translates to defective downstream signaling or antiviral responses after IFN-λ treatment in PLSCR1-deficient cells. This is particularly pertinent given the increase in IFN-λ ligand in vivo, which might compensate for receptor downregulation.

We agree with the reviewer that downstream activation of the IFN-λ signaling pathway is a critical aspect of PLSCR1’s proposed regulatory role. To investigate this, we attempted an ISRE-luciferase reporter assay to assess downstream signaling following IFN-λ treatment in PLSCR1 rescue cells. Unfortunately, the experiment encountered unforeseen technical issues. For additional context, please refer to our response to Reviewer #1’s public review #3.

(5) Detailed gating strategies for immune cell subsets are absent and should be included for clarity and reproducibility.

We would like to clarify that the immune cell subsets in BAL fluids were counted manually following cytospin preparation and Diff-Quik staining (Figure 2B and 7H, and Supplemental Figures 2C, 5D, and 8D), rather than by flow cytometry. We hope this resolves the reviewer’s confusion.

(6) The study does not definitively establish that reduced IFN-λ signaling causes the observed in vivo phenotype. Increased morbidity and mortality in PLSCR1-deficient mice could also stem from elevated TNF-α levels and lung damage, as proinflammatory cytokines and/or enhanced lung damage are known contributors to influenza morbidity and mortality. This point warrants detailed discussions.

We agreed with the reviewer that this study does not guarantee a definitive causality between reduced IFN-λ signaling and increased morbidity of Plscr1^-/- mice and more experiments are needed to reach the conclusion. We have acknowledged this limitation of our study in the “Discussion”, as requested by the reviewer. We hope to fully eliminate the confounding elements and definitively establish the proposed causality in future studies.

Reviewer #3 (Public review):

Summary:

Yang et al. have investigated the role of PLSCR1, an antiviral interferon-stimulated gene (ISG), in host protection against IAV infection. Although some antiviral effects of PLSCR1 have been described, its full activity remains incompletely understood.

This study now shows that Plscr1 expression is induced by IAV infection in the respiratory epithelium, and Plscr1 acts to increase Ifn-λr1 expression and enhance IFN-λ signaling possibly through protein-protein interactions on the cell membrane.

Strengths:

The study sheds light on the way Ifnlr1 expression is regulated, an area of research where little is known. The study is extensive and well-performed with relevant genetically modified mouse models and tools.

Weaknesses:

There are some issues that need to be clarified/corrected in the results and figures as presented.

Also, the study does not provide much information about the role of PLSCR1 in the regulation of Ifn-λr1 expression and function in immune cells. This would have been a plus.

We would like to thank the reviewer for the positive feedback and insightful comment regarding the roles of PLSCR1 and IFN-λR1 in immune cells. It is important to note that IFN-λR1 expression is highly restricted in immune cells and is primarily limited to neutrophils and dendritic cells[3]. While dendritic cells were not the focus of this study, we did examine all immune cell subsets in our single cell RNA seq data and performed infection experiments in Plscr1^floxStop/LysM-Cre⁺ mice. We have not observed any significant findings in these populations. On the other hand, we do have some interesting preliminary data suggesting a role for PLSCR1 in regulating Ifn-λr1 expression and function in neutrophils. These findings are discussed in detail in our response to reviewer #3’s recommendation #12.

Reviewer #3 (Recommendations):

(1) In Figure 1B, the Plscr1 label should be moved to the y-axis so that readers don't confuse it with the Plscr1-/- mice used in the other figure panels. The fact that WT mice were used should be added in the figure legend.

We apologize for the confusion in the figures. We have moved Plscr1 label to the y-axis in Figure 1B and have mentioned Wt mice were used in the figure legend.

(2) In Figure 1C and D, the type of dose leading to the presented data should be added to help the reader. Also, shouldn't statistics be added?

We appreciate the suggestion and have added doses to Figure 1C and 1D. We are confused about the request of adding statistics by the reviewer, as two-way ANOVA tests were used to compare weight losses, and the significance was labeled on the figures.

(3) In Figures 1, F, and G, it is not indicated whether sublethal or lethal dose was used for the IAV infection. This should be very clear in the figure and figure legend.

We apologize for the confusion of infection doses used in the figures. We have added doses to Figure 1F, 1G and 1H.

(4) In Figure 1, the CTCF abbreviation should be explained in the Figure legend.

We have explained CTCF in the figure legend as requested.

(5) In Figure 2B, this is percentages of what?

Figure 2B shows the percentages of each immune cell type within total BAL cells.

(6) In Figures 3A and B, transcriptomes for each condition are from how many mice? Also, what do heatmaps show? Fold induction, differences, etc, and from what? What is compared with what? In addition, is there a discordance between the RNAseq data of Figure 3A and the qPCR data of Fig. 3C in terms of Ifnlr1 expression?

In Figure 3A and 3C (previously 3B), RNA from the whole lungs of 9 mice per PBS-treated group and 4 mice per IAV-infected group were pooled for transcriptomic analysis. Figure 3A represents a heatmap of differential gene expression, while Figure 3C (previously 3B) represents fold changes in gene expression relative to uninfected controls. In both heatmaps, gene expression values are color-coded from row minimum (blue) to row maximum (red), enabling comparison across groups within each gene (row). The major comparison of interest in these heatmaps is between Wt infected mice versus Plscr1^-/- infected mice. We have added this information to the figure legend.

We also acknowledge the reviewer’s observation regarding the discordance between the RNA seq data of Figure 3A and the qPCR data of Figure 3B (previously 3C) for Ifnlr1 expression. To address this, we have repeated the qRT-PCR experiment with additional samples at 7 dpi. In the updated results, Wt mice consistently show significantly higher Ifn-λr1 expression than Plscr1^-/- infected mice at both 3 dpi and 7 dpi, consistent with the RNA seq data. However, a time-dependent discrepancy between the RNA-seq and qRT-PCR datasets remains: Ifn-λr1 expression continues to increase at 7 dpi in the RNA-seq data (Figure 3A), whereas it declines in the qRT-PCR results (Figure 3B). The reason for this discrepancy remains unclear and has been addressed in the Discussion section.

(7) In Figure 3D, have the authors checked whether the Ifnlr1 antibody they use is indeed specific for Ifnlr1? Have they used any blocking peptide for the anti-mouse Ifn-λr1 polyclonal antibody they are using? Also, in Figure 3E, the marker used for staining should be indicated in the pictures of the lung section.

Unfortunately, a blocking peptide is not available for the anti-mouse Ifn-λr1 polyclonal antibody used in our study. To assess antibody specificity, we have performed immunofluorescence staining of Ifn-λr1 on lung tissues from Ifn-λr1^-/- mice using the same antibody. No signal was detected (Supplemental Figure 5A), supporting the specificity of the antibody for Ifn-λr1.

As requested by the reviewer, we have added the marker (Ifn-λr1) to the pictures of the lung section in Figure 3E.

(8) In Figure 5, it's better to move each graph's label that stands to the top (e.g. PLSCR1, IFN-λR1 etc) to the y-axis label so that it doesn't get confused with the mouse -/- label.

We apologize for the confusion and have moved the top label to the y-axis in Figure 5.

(9) In Figure 6A, it is claimed that the 'two-dimensional UMAP demonstrated that these main lung cell populations (epithelial, endothelial, mesenchymal, and immune) were dynamic over the course of infection.'. This is not clear by the data. The percentage of cells per cluster should be calculated.

As requested by the reviewer, the proportion (Supplemental Figure 6A) and cell count (Supplemental Figure 6B) of each cluster have been calculated and included in “PLSCR1 Expression Is Upregulated in the Ciliated Airway Epithelial Compartment of Mice following Flu Infection” under “Results” section. Together with the two-dimensional UMAP (Figure 6A), these data demonstrate that the main lung cell populations (epithelial, endothelial, mesenchymal, and immune) were dynamic over the course of infection. Following infection, many populations emerged, particularly within the immune cell clusters. At the same time, some clusters were initially depleted and later restored, such as microvascular endothelial cells (cluster 2). Other populations, such as interferon-responsive fibroblasts (cluster 20), showed a dramatic yet transient expansion during acute infection and disappeared after infection resolved.

(10) In Figure 6 B and C, the legend should indicate that these are Violin plots. Also, if AT2 cells don't express Plscr1, does that indicate that in these cells Plscr1 is not needed for IFN-λR1 expression?

As requested, we have indicated in the legend of Figure 6B and 6C that these are violin plots. Plscr1 is expressed at low levels in AT2 cells. However, it is unclear whether Plscr1 is needed for Ifn-λr1 expression in AT2 cells, and it would be interesting to investigate further.

(11) In lines 302-304, it is stated that 'Among the various epithelial populations, ciliated epithelial cells not only had 303 the highest aggregated expression of Plscr1, but also were the only epithelial cell 304 population in which significantly more Plscr1 was induced in response to IAV infection.'. Which data/ figure support this statement?

Figure 6B shows that among the various epithelial populations, ciliated epithelial cells had the highest aggregated expression of Plscr1. To better illustrate this statement, we have rearranged the order of cell clusters from highest to lowest Plscr1 expression, and added red dots to indicate the mean expression levels for each cluster in Figure 6B.

Ciliated epithelial cells also had the most significant increase in Plscr1 expression (p < 2.22e-16 and p = 6.7e-05) in early IAV infection at 3 dpi (Figure 6C and Supplemental Figure 7A-7K). In comparison, AT1 cells were the only other epithelial cluster to show Plscr1 upregulation at 3dpi, but to a much less extent (p = 0.033, Supplemental Figure 7J). Supplemental Figure 7 was added to better support the statement and the explanation was added to “PLSCR1 Expression Is Upregulated in the Ciliated Airway Epithelial Compartment of Mice following Flu Infection” under “Results” section.

(12) As earlier, if Plscr1 is not expressed in neutrophils (Figure 6F), does that mean IFN-λR1 expression does not require Plscr1 in these cells?

Although Plscr1 is expressed at lower levels in neutrophils compared to epithelial cells, it is still detectable. In fact, our preliminary data suggest that IFN-λR1 expression in neutrophils is dependent on Plscr1. We have isolated neutrophils from peripheral blood and BAL of IAV-infected Wt and Plscr1^-/- mice using a mouse neutrophil enrichment kit. Quantitative PCR results showed that Plscr1^-/- neutrophils exhibit significantly lower expression of Ifn-λr1, alongside elevated levels of Il-1β, Il-6 and Tnf-α in IAV infection (see figures below). These findings suggest that Plscr1 may play an anti-inflammatory role in neutrophils by upregulating Ifn-λr1. These data were not included in the current manuscript because they are beyond the scope of current study, but we hope to address the role of PLSCR1 in regulating IFN-λR1 expression and function in neutrophils in a future study.

Author response image 3.

(13) The Figure 7A legend is not well stated. Something like ' Schematic representation of the experimental design of...' should be included. Also, Figure 7J is not referenced in the text.

We apologize for the unclear Figure 7A legend and have changed it to “Schematic representation of the experimental design of ciliated epithelial cell conditional Plscr1 KI mice.” Figure 8 (previously Figure 7J) has now been referenced in the text.

(14) In the Methods, more specific information in some parts should be provided. For example, the clones of the antibodies used should be included.

Apart from the 10x technology, the kits used and the type of the Illumina sequencing should be provided. Information on how the QC was performed (threshold for reads/cell, detected genes/per cells, and % of mitochondrial genes etc) should be added.

We apologize for the missing information in the “Methods”. We have now provided the clones of the antibodies used, the kit used to generate single-cell transcriptomic libraries, the type of the Illumina sequencing, and the QC performance data.

References

(1) Rusinova, I., et al., Interferome v2.0: an updated database of annotated interferon-regulated genes. Nucleic Acids Res, 2013. 41(Database issue): p. D1040-6.

(2) Xu, D., et al., PLSCR1 is a cell-autonomous defence factor against SARS-CoV-2 infection. Nature, 2023. 619(7971): p. 819-827.

(3) Donnelly, R.P., et al., The expanded family of class II cytokines that share the IL-10 receptor-2 (IL-10R2) chain. J Leukoc Biol, 2004. 76(2): p. 314-21.

Author response:

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

Reviewer #1 (Public Review):

Here the authors discuss mechanisms of ligand binding and conformational changes in GlnBP (a small E Coli periplasmic binding protein, which binds and carries L-glutamine to the inner membrane ATP-binding cassette (ABC) transporter). The authors have distinguished records in this area and have published seminal works. They include experimentalists and computational scientists. Accordingly, they provide comprehensive, high-quality, experimental and computational work. They observe that apo- and holo- GlnBP does not generate detectable exchange between open and (semi-) closed conformations on timescales between 100 ns and 10 ms. Especially, the ligand binding and conformational changes in GlnBP that they observe are highly correlated. Their analysis of the results indicates a dominant induced-fit mechanism, where the ligand binds GlnBP prior to conformational rearrangements. They then suggest that an approach resembling the one they undertook can be applied to other protein systems where the coupling mechanism of conformational changes and ligand binding. They argue that the intuitive model where ligand binding triggers a functionally relevant conformational change was challenged by structural experiments and MD simulations revealing the existence of unliganded closed or semi-closed states and their dynamic exchange with open unbound conformations, discuss alternative mechanisms that were proposed, their merits and difficulties, concluding that the findings were controversial, which, they suggest is due to insufficient availability of experimental evidence to distinguish them. As to further specific conclusions they draw from their results, they determine that a conformational selection mechanism is incompatible with their results, but induced fit is. They thus propose induced fit as the dominant pathway for GlnBP, further supported by the notion that the open conformation is much more likely to bind substrate than the closed one based on steric arguments. Considering the landscape of substrate-free states, in my view, the closed state is likely to be the most stable and, thus most highly populated. As the authors note and I agree that state can be sterically infeasible for a deep-pocketed substrate. As indeed they also underscore, there is likely to be a range of open states. If the populations of certain states are extremely low, they may not be detected by the experimental (or computational) methods. The free energy landscape of the protein can populate all possible states, with the populations determined by their relative energies. In principle, the protein can visit all states. Whether a particular state is observed depends on the time the protein spends in that state. The frequencies, or propensities, of the visits can determine the protein function. As to a specific order of events, in my view, there isn't any. It is a matter of probabilities which depend on the populations (energies) of the states. The open conformation that is likely to bind is the most favorable, permitting substrate access, followed by minor, induced fit conformational changes. However, a key factor is the ligand concentration. Ligand binding requires overcoming barriers to sustain the equilibrium of the unliganded ensemble, thus time. If the population of the state is low, and ligand concentration is high (often the case in in vitro experiments, and high drug dosage scenarios) binding is likely to take place across a range of available states. This is however a personal interpretation of the data. The paper here, which clearly embodies massive careful, and high-quality work, is extensive, making use of a range of experimental approaches, including isothermal titration calorimetry, single-molecule Förster resonance energy transfer, and surface-plasmon resonance spectroscopy. The problem the authors undertake is of fundamental importance.

Reviewer #2 (Public Review):

The manuscript by Han et al and Cordes is a tour-de-force effort to distinguish between induced fit and conformational selection in glutamine binding protein (GlnBP). 

We thank the referee for the recognition of the work and effort that has gone into this manuscript. 

It is important to say that I don't agree that a decision needs to be made between these two limiting possibilities in the sense that whether a minor population can be observed depends on the experiment and the energy difference between the states. That said, the authors make an important distinction which is that it is not sufficient to observe both states in the ligand-free solution because it is likely that the ligand will not bind to the already closed state. The ligand binds to the open state and the question then is whether the ligand sufficiently changes the energy of the open state to effectively cause it to close. The authors point out that this question requires both a kinetic and a thermodynamic answer. Their "method" combines isothermal titration calorimetry, single-molecule FRET including key results from multi-parameter photon-by-photon hidden Markov modelling (mpH2MM), and SPR. The authors present this "method" of combination of experiments as an approach to definitively differentiate between induced fit and conformational selection. I applaud the rigor with which they perform all of the experiments and agree that others who want to understand the exact mechanism of protein conformational changes connected to ligand binding need to do such a multitude of different experiments to fully characterize the process. However, the situation of GlnBP is somewhat unique in the high affinity of the Gln (slow offrate) as compared to many small molecule binding situations such as enzyme-substrate complexes. It is therefore not surprising that the kinetics result in an induced fit situation. 

For us these comments are an essential part of the conceptual aspects of our work and the resulting research. From a descriptive viewpoint, it is essential for us (and we tried to further highlight and stress this in the updated version of our paper) that IF and CS are two kinetic mechanisms of ligand binding. They imply – if active in a biomolecular system – a temporal order and timescale separation of ligand binding and conformational changes. Since we found many conflicting results for the binding mechanism of GlnBP, but also other SPBs, we decided to assess the situation in GlnBP. 

In the case of the E-S complexes I am familiar with, the dissociation is much more rapid because the substrate binding affinity is in the micromolar range and therefore the re-equilibration of the apo state is much faster. In this case, the rate of closing and opening doesn't change much whether ligand is present or not. Here, of course, once the ligand is bound the re-equilibration is slow. Therefore, I am not sure if the conclusions based on this single protein are transferrable to most other protein-small molecule systems. 

We do not argue that our results and interpretations are valid for most other protein-ligand systems may those be enzymes or simple ligand binders. Yet, based on the conservation of ABC-related SBPs and the fact that quite a few of them show sub-µM Kds, we render it likely to find many analogous situations as for GlnBP also based on our previous results e.g., from de Boer et al., eLife (2019).

I am also not sure if they are transferrable to protein-protein systems where both molecules the ligand and the receptor are expected to have multiscale dynamics that change upon binding.

As we argue above the two mechanisms IF/CS imply a clear temporal order and separation of timescales for ligand binding and conformational changes. These mechanisms are simple and extreme cases that we tested before more complex kinetic schemes are inferred for the description of ligand binding and conformational changes (which might not be necessary). 

Strengths:

The authors provide beautiful ITC data and smFRET data to explore the conformational changes that occur upon Gln binding. Figure 3D and Figure 4 (mpH2MM data) provide the really critical data. The multi-parameter photon-by-photon hidden Markov modelling (mpH2MM) data. In the presence of glutamine concentrations near the Kd, two FRET-active sub-populations are identified that appear to interconvert on timescales slower than 10 ms. They then do a whole bunch of control experiments to look for faster dynamics (Figure 5). They also do TIRF smFRET to try to compare their results to those of previous publications. Here, they find several artifacts are occurring including inactivation of ~50% of the proteins. They also perform SPR experiments to measure the association rate of Gln and obtain expectedly rapid association rates on the order of 10^{^}8 M-1s-1.

Thank you.  

Weaknesses:

Looking at the traces presented in the supplementary figures, one can see that several of the traces have more than one molecule present. The authors should make sure that they use only traces with a single photobleaching event for each fluorophore. One can see steps in some of the green traces that indicate two green fluorophors (likely from 2 different molecules) in the traces. This is one of the frequent problems with TIRF smFRET with proteins, that only some of the spots represent single molecules and the rest need to be filtered out of the analysis.

We have inspected all TIRF data provided with the manuscript and assume that the referee refers to data shown in current Appendix Figure 4/5. We agree that those traces in which no photo bleaching occurs could potentially be questioned, yet they would not change our interpretations and thus decided to leave the figure as is.

The NMR experiments that the authors cite are not in disagreement with the work presented here. NMR is capable of detecting "invisible states" that occur in 1-5% of the population. SmFRET is not capable of detecting these very minor states. I am quite sure that if NMR spectroscopists could add very high concentrations of Gln they would also see a conversion to the closed population.

We agree with the referee that NMR is capable of detecting invisible states that occur in 1-5% of the population (see e.g., the paper cited in our manuscript by Tang, C et al., Open-to-closed transition in apo maltose-binding protein observed by paramagnetic NMR. Nature 2007, 449, 1078). Yet, we see a strong disagreement between our work and papers on GlnBP, where a combination of NMR, FRET and MD was used (Feng, Y. et al., Conformational Dynamics of apo‐GlnBP Revealed by Experimental and Computational Analysis. Angewandte Chemie 2016, 55, 13990; Zhang, L. et al., Ligand-bound glutamine binding protein assumes multiple metastable binding sites with different binding affinities. Communications biology 2020, 3, 1). These inconsistencies were also noted by others in the field (Kooshapur, H. et al., NMR Analysis of Apo Glutamine‐Binding Protein Exposes Challenges in the Study of Interdomain Dynamics. Angewandte Chemie 2019, 58, 16899) and we reemphasize that this latest NMR publication comes to similar conclusions as we present in our manuscript.   

Reviewer #1 (Recommendations For The Authors):

The paper embodies massive careful and high-quality work, and is extensive, making use of a range of experimental approaches, including isothermal titration calorimetry, single-molecule Förster resonance energy transfer, and surface-plasmon resonance spectroscopy. Considering this extensiveness, I do not see what more the authors can do.

We very much appreciate the assessment and positive comments of the referee, but still tried to incorporate simulation data to support our interpretations.

Reviewer #2 (Recommendations For The Authors):

(1) Looking at the traces presented in the supplementary figures, one can see that several of the traces have more than one molecule present. The authors should make sure that they use only traces with a single photobleaching event for each fluorophore. One can see steps in some of the green traces that indicate two green fluorophors (likely from 2 different molecules) in the traces. This is one of the frequent problems with TIRF smFRET with proteins, that only some of the spots represent single molecules and the rest need to be filtered out of the analysis.

See response above for iteration of TIRF data selection and analysis.

(2) The NMR experiments that the authors cite are not in disagreement with the work presented here. NMR is capable of detecting "invisible states" that occur in 1-5% of the population. SmFRET is not capable of detecting these very minor states. I am quite sure that if NMR spectroscopists could add very high concentrations of Gln they would also see a conversion to the closed population.

See response above.

Minor point:

(1) It is difficult to see what is going on between apo and holo in Figure 1B. Could the authors make Figure 1a, 1b apo, and 1b holo in the same orientation (by aligning D2 or D1 to each other in all figures) so one can see which helices are in the same place and which have moved?

We respectfully disagree and decided to keep this figure as it is

Author response:

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

Reviewer #1 (Public review):

Summary:

This study focuses on the bacterial metabolite TMA, generated from dietary choline. These authors and others have previously generated foundational knowledge about the TMA metabolite TMAO, and its role in metabolic disease. This study extends those findings to test whether TMAO's precursor, TMA, and its receptor TAAR5 are also involved and necessary for some of these metabolic phenotypes. They find that mice lacking the host TMA receptor (Taar5-/-) have altered circadian rhythms in gene expression, metabolic hormones, gut microbiome composition, and olfactory and innate behavior. In parallel, mice lacking bacterial TMA production or host TMA oxidation have altered circadian rhythms.

Strengths:

These authors use state-of-the-art bacterial and murine genetics to dissect the roles of TMA, TMAO, and their receptor in various metabolic outcomes (primarily measuring plasma and tissue cytokine/gene expression). They also follow a unique and unexpected behavioral/olfactory phenotype. Statistics are impeccable.

Weaknesses:

Enthusiasm for the manuscript is dampened by some ambiguous writing and the presentation of ideas in the introduction, both of which could easily be improved upon revision.

We apologize for the abbreviated and ambiguous writing style in our original submission. Given Reviewer 2 also suggested reorganizing and rewriting certain parts, we have spent time to remove ambiguity by adding additional points of clarification and adding more historical context to justify studying TMA-TAAR5 signaling in regulating host circadian rhythms. We have also reorganized the presentation of data aligned with this.

Reviewer #2 (Public review):

Summary:

In the manuscript by Mahen et al., entitled "Gut Microbe-Derived Trimethylamine Shapes Circadian Rhythms Through the Host Receptor TAAR5," the authors investigate the interplay between a host G protein-coupled receptor (TAAR5), the gut microbiota-derived metabolite trimethylamine (TMA), and the host circadian system. Using a combination of genetically engineered mouse and bacterial models, the study demonstrates a link between microbial signaling and circadian regulation, particularly through effects observed in the olfactory system. Overall, this manuscript presents a novel and valuable contribution to our understanding of hostmicrobe interactions and circadian biology. However, several sections would benefit from improved clarity, organization, and mechanistic depth to fully support the authors' conclusions.

Strengths:

(1) The manuscript addresses an important and timely topic in host-microbe communication and circadian biology.

(2) The studies employ multiple complementary models, e.g., Taar5 knockout mice, microbial mutants, which enhance the depth of the investigation.

(3) The integration of behavioral, hormonal, microbial, and transcript-level data provides a multifaceted view of the observed phenotype.

(4) The identification of olfactory-linked circadian changes in the context of gut microbes adds a novel perspective to the field.

Weaknesses:

While the manuscript presents compelling data, several weaknesses limit the clarity and strength of the conclusions.

(1) The presentation of hormonal, cytokine, behavioral, and microbiome data would benefit from clearer organization, more detailed descriptions, and functional grouping to aid interpretation.

We appreciate this comment and have reorganized the data to improve functional grouping and readability. We have also added additional detail to descriptions of the data in the revised figure legends and results.

(2) Some transitions-particularly from behavioral to microbiome data-are abrupt and would benefit from better contextual framing.

We agree with this comment, and have added additional language to provide smoother transitions. This in many cases brings in historical context of why we focused on both behavioral and microbiome alterations in this body of work.

(3) The microbial rhythmicity analyses lack detail on methods and visualization, and the sequencing metadata (e.g., sample type, sex, method) are not clearly stated.

We apologize for this, and have now added more detail in our methods, figures, and figure legends to ensure the reader can easily understand sample type, sex, and the methods used. 

(4) Several figures are difficult to interpret due to dense layouts or vague legends, and key metabolites and gene expression comparisons are either underexplained or not consistently assessed across models.

Aligned with the last comment we now added more detail in our methods, figures, and figure legends to provide clear information. We have now provided additional data showing the same key metabolites, hormones, and gene expression alterations in each model if the same endpoints were measured.

(5) Finally, while the authors suggest a causal role for TAAR5 and its ligand in circadian regulation, the current data remain correlative; mechanistic experiments or stronger disclaimers are needed to support these claims.

We agree with this comment, and as a result have removed any language causally linking TMA and TAAR5 together in circadian regulation. Instead, we only state finding in each model and refrain from overinterpreting.

Reviewer #3 (Public review):

Summary:

Deletion of the TMA-sensor TAAR5 results in circadian alterations in gene expression, particularly in the olfactory bulb, plasma hormones, and neurobehaviors.

Strengths:

Genetic background was rigorously controlled.

Comprehensive characterization.

Weaknesses:

The weaknesses identified by this reviewer are minor.

Overall, the studies are very nicely done. However, despite careful experimentation, I note that even the controls vary considerably in their gene expression, etc, across time (eg, compare control graphs for Cry 1 in IB, 4B). It makes me wonder how inherently noisy these measurements are. While I think that the overall point that the Taar5 KO shows circadian changes is robust, future studies to dissect which changes are reproducible over the noise would be helpful.

We thank the reviewer for this insightful comment. We completely agree that there are clear differences in the circadian data in experiments from Taar5^-/- mice and those from gnotobiotic mice where we have genetically deleted CutC. Although the data from Taar5^-/- mice show nice robust circadian rhythms, the data from mice where microbial CutC is altered have inherently more “noise”. We attribute some of this to the fact that the Taar5^-/- mouse experiment have a fully intact and diverse gut microbiome . Whereas, the gnotobiotic study with CutC manipulation includes only a 6 member microbiome community that does not represent the normal microbiome diversity in the gut. This defined synthetic community was used as a rigorous reductionist approach, but likely affected the normal interactions between a complex intact gut microbiome and host circadian rhythms. We have added some additional discussion to indicate this in the limitations section of the manuscript.

Impact:

These data add to the growing literature pointing to a role for the TMA/TMAO pathway in olfaction and neurobehavioral.

Reviewer #1 (Recommendations for the authors):

I suggest a revision of the writing and organization. The potential impact of the study after reading the introduction is unclear. One example, in the intro, " TMAO levels are associated with many human diseases including diverse forms of CVD5-12, obesity13,14, type 2 diabetes15,16, chronic kidney disease (CKD)17,18, neurodegenerative conditions including Parkinson's and Alzheimer's disease19,20, and several cancers21,22" It would be helpful to explain how the previous literature has distinguished that the driver of these phenotypes is TMA/TMAO and not increased choline intake. Basically, for a TMA/O novice reader, a more detailed intro would be helpful.

We appreciate this insightful comment and have now provided a more expansive historical context for the reader regarding the effects of choline consumption (which impacts many things, including choline, acetylcholine, phosphatidylcholine, TMA, TMAO, etc) versus the primary effects of TMA and TMAO.

There were also many uses of vague language (regulation/impact/etc). Directionality would be super helpful.

We thank the reviewer for this recommendation and have improved language as suggested to show directionality of our findings. The terms regulation, impact, shape etc. are used only when we describe multiple variable changing at the same time over the time course of a 24-hour circadian period (some increased and some decreased).

Reviewer #2 (Recommendations for the authors):

In the manuscript by Mahen et al., entitled "Gut Microbe-Derived Trimethylamine Shapes Circadian Rhythms Through the Host Receptor TAAR5," the authors investigate the interplay between a host G protein-coupled receptor (TAAR5), the gut microbiota-derived metabolite trimethylamine (TMA), and the host circadian system. Using a combination of genetically engineered mouse and bacterial models, the study demonstrates a link between microbial signaling and circadian regulation, particularly through effects observed in the olfactory system. Overall, this manuscript presents a novel and valuable contribution to our understanding of hostmicrobe interactions and circadian biology. However, several sections would benefit from improved clarity, organization, and mechanistic depth to fully support the authors' conclusions. Below are specific major and minor suggestions intended to enhance the presentation and interpretation of the data.

Major suggestions:

(1) Consider adding a schematic/model figure as Panel A early in the manuscript to help readers understand the experimental conditions and major comparisons being made.

We thank the reviewer for this recommendation and have added a graphical abstract figure to help the reader understand the major comparisons being made. 

(2) Could the authors present body weight and food intake characteristics in Taar5 KO vs. WT animals?

We have added body weight data as requested in Figure 1, Figure supplement 1. Although we have not stressed these mice with a high fat diet for these behavioral studies, under chow-fed conditions studied here we did not find any significant differences in body weight. Given no difference in body weight, we did not collect data on food consumption and have mentioned this as a limitation in the discussion.  

(3) Several figures, especially Figures 3 and 4, and Supplemental Figures, would benefit from more structured organization and expanded legends. Grouping related data into thematic panels (e.g., satiety vs. appetite hormones, behavioral domains) may help improve readability.

We appreciate the reviewer’s thoughtful comments and agree that reorganization would improve clarity. We have reorganized figures to improve clarity and have expanded the figure legends to provide more detail on experimental methods. 

(4) Clarify and expand the description of hormonal and cytokine changes. For instance, the phrase "altered rhythmic levels" is vague - do the authors mean dampened, phase-shifted, enhanced, etc., relative to WT controls?

Given a similar suggestion was made by Reviewer 1, we have provided more precise language focused on directionality and which specific endpoints we are referring to. For anything looking at circadian rhythms, the revised manuscript includes specific indications when we are discussing mesor, amplitude, and acrophase alterations. The terms regulation, impact, shape etc. are used only when we describe multiple complex variables changing at the same time over the time course of a 24-hour circadian period (some increased and some decreased).

(5) Consider grouping hormones and cytokines functionally (e.g., satiety vs. appetite-stimulating, pro- vs. antiinflammatory) to better interpret how these changes relate to the KO phenotype.

We thank the reviewer for this recommendation, and have re-organized figure panels to reflect this.

(6) Please provide a more detailed description of the behavioral results, particularly those in Supplemental Figure 2.

We have both expanded the methods description in the revised figure legends, but have also added a more detailed description of the behavioral results.

(7) As with hormonal data, behavioral outcomes would be easier to follow if organized thematically (e.g., locomotor activity, anxiety-like behavior, circadian-related behavior), especially for readers less familiar with behavioral assays.

We appreciate this reviewer’s comment and agree that we can better group our data to show how each test is associated with the type of behavior it assesses. As a result we have reorganized the behavioral data into broad categories such as olfactory-related, innate, cognitive, depressive/anxiety-like, or social behaviors. We have also new data in each of these behavioral categories to provide a more comprehensive understanding of behavioral alterations seen in Taar5^-/- mice.

(8) The following statement needs clarification: "Also, it is important to note that many behavioral phenotypes examined, including tests not shown, were unaltered in Taar5-/- mice (Figures S2G, S2H, and S2I)." Consider rephrasing to explicitly state the intended message: are the authors emphasizing a lack of behavioral phenotype, or highlighting specific unaltered aspects?

We apologize for this confusing statement, and have changed the verbiage to improve readability. To expand the comprehensive nature of this study, we also now include the tests that were “not shown” in the original submission to provide a more comprehensive understanding of behavioral alterations seen in Taar5^-/- mice. These new data are included as 6 different figure supplements to main Figure 2.

(9) The transition from behavior to microbiome data feels abrupt. Can the authors better explain whether the behavioral changes are thought to result from gut microbial function, independent of TMA-Taar5 signaling?

We apologize for the poor transitions in our writing style. We have spent time to explain the previous findings linking the TMA pathway to circadian reorganization of the gut microbiome (mostly coming from our original paper Schugar R, et al. 2022, eLife) and how this correlates with behavioral phenotypes. Although at this point it is difficult to know whether the microbiome changes are driving behavioral changes, or vice versa it could be central TAAR5 signaling is altering oscillations in gut microbiome, we present our findings here as a framework for follow up studies to more precisely get at these questions. It is important to note that our experiment using defined community gnotobiotic mice with or without the capacity to produce TMA (i.e. CutC-null community) shows that clearly microbial TMA production can impact host circadian rhythms in the olfactory bulb. Additional experiments beyond the scope of this work will be required to test which phenotypes originate from TMA-TAAR5 signaling versus more broad effects of the restructured gut microbiome.

(10) For Figure 3A, please expand the microbiome results with more granularity:

(a) Indicate in the Results section whether the sequencing method was 16S amplicon or metagenomic.

Sequencing was done using 16S rRNA amplicon sequencing using methods published by our group (PMID: 36417437, PMID: 35448550).

(b) State whether samples were from males, females, or a mix. 

We have indicated that all mice from Figure 1 were male mice in the revised figure legend.

(c) Clarify whether beta diversity is based on phylogenetic or non-phylogenetic metrics. Consider using both  types if not already done.

Beta diversity was analyzed using the Bray-Curtis dissimilarity index as the metric. Details have been included in the methods section.

(d) Make lines partially transparent in the Beta-diversity plot so that individual points are visible.

We have now updated the Beta-diversity plot with individual points visualized.

(e) Clarify what percentage of variation in the Beta-diversity plot is explained by CCA1, and whether this low percentage suggests minimal community-level differences.

We have updated the Beta-diversity plot to include the R² and p-values associated with these data.

(f) Confirm if the y-axis on the Beta-diversity plot should be labeled CCA2 rather than "CCAA 1".

We appreciate this comments, given it identified a typographical error in the plot. The revised figure now include the proper label of CCA2 instead of CCAA 1.

(11) For Figure 3B:

(a) Provide a description of the taxonomy plot in the results.

We have added a description of the taxonomy plot in the revised results section.

(b) Add phylum-level labels and enlarge the legend to improve the readability of genus-level data.

We agree this is a good suggestion so have enlarged the legend for the genus-level data and have also added phylum-level plots as well in the revised manuscript in Figure 3, figure supplement 1.

(12) Rhythmicity of the microbiome is central to the manuscript. The current approach of comparing relative abundance at discrete time points is limiting.

We thank the reviewer for this comment. We agree with this statement that discrete timepoint are not enough to describe circadian rhythmicity. In addition to comparing genotypes at discrete time points, we also used a rigorous cosinor analysis to plot the data over a 24-hour time period, and those differences are shown in the figure itself as well as Table 1. 

(a) Please describe how rhythmicity was determined, e.g., what data or statistical method supports the statement: "Taar5-/- mice showed loss of the normal rhythmicity for Dubosiella and Odoribacter genera yet gained in amplitude of rhythmicity for Bacteroides genera (Figure 3 and S3)."

We appreciate this reviewer comment. Rhythmicity was determined using a cosinor analysis by use of an R program. Cosinor analysis is a statistical method used to model and analyze rhythmic patterns in time-series data, typically assuming a sinusoidal (cosine) shape. It estimates key parameters like mesor (mean level), amplitude (height of oscillation), and acrophase (timing of the peak), making it especially useful in fields like chronobiology and circadian rhythm research. We have used this in previous research to describe circadian rhythms. We do plan to improve language considering directionality of these circadian changes. 

(b) Supplemental Figure S3 needs reorganization to highlight key findings. It's not currently clear how taxa are arranged or what trends are being shown.

The data in Figure S3 show the entire 24-hour time course of the cecal taxa that were significantly altered for at least one time point between Taar5^+/+ and Taar5^-/- mice. Given we showed time pointspecific alterations in the Main Figure 3, we thought these more expansive plots would be important to show to depict how the circadian rhythms were altered.

(c) Supplemental Table 1, which includes 16S features, should be referenced and discussed in the microbiome section.

We have now referenced and discussed Supplemental Table 1 which includes all cosinor statistics for microbiome and other data presented in circadian time point studies.

(13) Did the authors quantify the 16S rRNA gene via RT-PCR to determine if this was similar between KO and WT over the 24-hour period?

We did not quantify 16S rRNA gene via RT-PCR, but do not think adding this will change our overall interpretations.

(14) Reorganize Figure 4 to align with the order of results discussed-starting with TMA and TMAO, followed by related metabolites like choline, L-carnitine, and gamma-butyrobetaine.

We thank the reviewer for this comment. We have chosen this organization because it is ordered from substrates (choline, L-carnitine, and betaine) to the microbe-associated products (TMA then TMAO). We will improve the writing associated with this figure to clearly explain this organization.

(a) Although the changes in the latter metabolites are more modest, they may still have physiological relevance. Could the authors comment on their significance?

We appreciate this reviewer comment and agree. We have expanded the results and discussion to address this.

(15) The authors note similarities in circadian gene expression between Taar5 KO mice and Clostridium sporogenes WT vs. ΔcutC mice, but the gene patterns are not consistent.

(a) Can the authors clarify what conclusions can reasonably be drawn from this comparison?

We hesitate to make definitive conclusions in the manuscript on why the gene patterns are not consistent, because it would be speculation. However, one major factor likely driving differences is the status of the diversity of the gut microbiome in the different studies. For instance, in the studies using Taar5^+/+ and Taar5^-/- mice there is a very diverse microbiome in these conventionally housed mice. In contrast, by design the experiment using Clostridium sporogenes WT vs. ΔcutC communities is a reductionist approach that allows us to genetically define TMA production. In these gnotobiotic mice, the simplified community has very limited diversity and this likely alters the host circadian rhythms in gene expression quite dramatically. Although it is impossible to directly compare the results between these experiments given the difference microbiome diversity, there are clearly alterations in host gene expression when we manipulate TMA production (i.e. ΔcutC community) or TMA sensing (i.e. Taar5^-/-). 

(16) Were circadian and metabolic genes (e.g., Arntl, Cry1, Per2, Pemt, Pdk4) also analyzed in brown adipose tissue of Taar5 KO mice, and how do these results compare to the Clostridium models?

We thank the reviewer for this comment. Unfortunately, we did not collect brown adipose tissue in our original Taar5 study. We plan on doing this in future follow up studies studying cold-induced thermogenesis that are beyond the scope of this manuscript. However, we have decided to include data from our two timepoint Taar5 study which looks at ZT2 (9am) and ZT14 (9pm). There are clear differences in circadian genes between these timepoints. 

(17) To allow a more direct comparison, please ensure the same cytokines (e.g., IL-1β, IL-2, TNF-α, IFN-γ, IL6, IL-33) are reported for both the Taar5 KO and microbial models.

We thank the reviewer for this comment and now include data from the same cytokines for each study.

(18) What was the defined microbial community used to colonize germ-free mice with C. sporogenes strains? Did this community exhibit oscillatory behavior?

To define TMA levels using a genetically-tractable model of a defined microbial community, we leveraged access to the community originally described by our collaborator Dr. Federico Rey (University of Wisconsin – Madison) (PMID: 25784704). We chose this community because it provide some functional metabolic diversity and is well known to allow for sufficient versus deficient TMA production. We are thankful for the reviewer comments about oscillatory behavior of this defined community, and to be responsive have performed sequencing to detect the species over time. These data are now included in the revised manuscript and show that there are clear differences in the oscillatory behavior of the defined community members. These data provide additional support that bacterial TMA production not only alters host circadian rhythms, but also the rhythmic behavior of gut bacteria themselves which has never been described before.

(19) Can the authors explain the rationale for measuring additional metabolites such as tryptophan, indole acetic acid, phenylacetic acid, and phenylacetylglycine? How are these linked to CutC gene function or Taar5 signaling?

We appreciate that this could be confusing, but have included other gut microbial metabolites to be as comprehensive as possible. This is important to include because we have found in other gnotobiotic studies where we have genetically altered metabolite production, if we alter one gut microbe-derived metabolite there can be unexpected alterations in other distinct classes of microbe-derived metabolites (PMID: 37352836). This is likely due to the fact that complex microbe-microbe and microbehost interactions work together to define systemic levels of circulating metabolites, influencing both the production and turnover of distinct and unrelated metabolites.

(20) The authors make several strong claims suggesting that loss of Taar5 or disruption of its ligand directly alters the circadian gene network. However, the current data are correlative. The authors should clarify that these findings demonstrate associations rather than direct causal effects, unless additional mechanistic evidence is provided. Approaches such as studies conducted in constant darkness, measurements of wheelrunning behavior, or analyses that control for potential confounding factors, e.g., inflammation or metabolic disruption, would help establish whether the observed changes in clock gene expression are primary or secondary effects. The authors are encouraged to either soften these causal claims or acknowledge this limitation explicitly in the discussion.

We thank the reviewer for this comment. We agree and have softened our language about direct effects of TMA via TAAR5 because we agree the data presented here are correlative only. 

Minor suggestions:

(1) Avoid repetitive phrases such as "it is important to note..." for improved flow. Rephrasing these instances will enhance readability.

We thank the reviewer for this suggestion and have deleted such repetitive phrases.  

(2) For Figure 2, remove interpretations above he graphs and use simple, descriptive panel labels, similar to those in Supplemental Figure 2.

We have removed these interpretations as suggested, but have retained descriptive panel labels to help the reader understand what type of data are being presented.

Reviewer #3 (Recommendations for the authors):

Minor:

In Figure 1D, UCP1 does not appear to be significantly changed.

We thank the reviewer for this comment and agree that UCP1 gene expression is not significantly altered . However, given the key role that UCP1 plays in white adipose tissue beiging, which is suppressed by the TMAO pathway, we think it is critical to show that this effect appears unaffected by perturbed TMA-TAAR5 signaling.

It would be helpful, in the discussion, to summarize any consistent changes across Taar5 KO, CutC deletion, and FMO3 deletion.

We have added this to the discussion, but as discussed above we hesitate to make strong interpretations about consistency between the models because the microbiome diversity is so different between the studies, and we did not measure all endpoints in both models.

For the Cosinor analysis, it may be helpful to remove the p-values that are >0.05 from the figures.

We have now removed any non-significant p-values that are associated with our figures. 

For Figure 2, Supplement 1E, what are the two bars for each genotype?

We appreciate the reviewer pointing this out and will further explain this test in the figure with labels and in the legend.

Author response:

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

Editors comments:

I would encourage you to submit a revised version that addresses the following two points:

[a] The point from Reviewer #1 about a possible major confounding factor. The following article might be germane here: Baas and Fennell, 2019: https://papers.ssrn.com/sol3/papers.cfm?abstract_id=3339568

I don’t believe that the point raised by reviewer 1 is a confounder, see my response below.

This article highlighted was in my reading list, but I did not cite it because I was confused by its methods.

The point from Reviewer #4 about the abstract. It is important that the abstract says something about how reviewers reacted to the original versions of articles in which they were cited (ie, the odds ratio = 0.84, etc result), before going on to discuss how they reacted to revised articles (ie, the odds ratio = 1.61, etc result). I would suggest doing this along the following lines - but please feel free to reword the passage "but this effect was not strong/conclusive":

When reviewers were cited in the original version of the article under review, they were less likely to approve the article compared with reviewers who were not cited, but this effect was not strong/conclusive (odds ratio = 0.84; adjusted 99.4% CI: 0.69-1.03). However, when reviewers were cited in the revised version of the article, they were more likely to approve compared with reviewers who were not cited (odds ratio = 1.61; adjusted 99.4% CI: 1.16-2.23).

I have changed the abstract to include the odds ratios for version 1 and have used the same wording as from the main text.

Reviewer #1 (Public review):

Summary:

The work used open peer reviews and followed them through a succession of reviews and author revisions. It assessed whether a reviewer had requested the author include additional citations and references to the reviewers' work. It then assessed whether the author had followed these suggestions and what the probability of acceptance was based on the authors decision. Reviewers who were cited were more likely to recommend the article for publication when compared with reviewers that were not cited. Reviewers who requested and received a citation were much likely to accept than reviewers that requested and did not receive a citation.

Strengths and weaknesses:

The work's strengths are the in-depth and thorough statistical analysis it contains and the very large dataset it uses. The methods are robust and reported in detail.

I am still concerned that there is a major confounding factor: if you ignore the reviewers requests for citations are you more likely to have ignored all their other suggestions too? This has now been mentioned briefly and slightly circuitously in the limitations section. I would still like this (I think) major limitation to be given more consideration and discussion, although I am happy that it cannot be addressed directly in the analysis.

This is likely to happen, but I do not think it’s a confounder. A confounder needs to be associated with both the outcome and the exposure of interest. If we consider forthright authors who are more likely to rebuff all suggestions, then they would receive just as many citation and self-citation requests as authors who were more compliant. The behaviour of forthright authors would likely only reduce the association seen in most authors which would be reflected in the odds ratios.

Reviewer #2 (Public review):

Summary:

This article examines reviewer coercion in the form of requesting citations to the reviewer's own work as a possible trade for acceptance and shows that, under certain conditions, this happens.

Strengths:

The methods are well done and the results support the conclusions that some reviewers "request" self-citations and may be making acceptance decisions based on whether an author fulfills that request.

Weakness:

I thank the author for addressing my comments about the original version.

Reviewer #3 (Public review):

Summary:

In this article, Barnett examines a pressing question regarding citing behavior of authors during the peer review process. In particular, the author studies the interaction between reviewers and authors, focusing on the odds of acceptance, and how this may be affected by whether or not the authors cited the reviewers' prior work, whether the reviewer requested such citations be added, and whether the authors complied/how that affected the reviewer decision-making.

Strengths:

The author uses a clever analytical design, examining four journals that use the same open peer review system, in which the identities of the authors and reviewers are both available and linkable to structured data. Categorical information about the approval is also available as structured data. This design allows a large scale investigation of this question.

Weaknesses:

My original concerns have been largely addressed. Much more detail is provided about the number of documents under consideration for each analysis, which clarifies a great deal.

Much of the observed reviewer behavior disappears or has much lower effect sizes depending on whether "Accept with Reservations" is considered an Accept or a Reject. This is acknowledged in the results text. Language has been toned down in the revised version.

The conditional analysis on the 441 reviews (lines 224-228) does support the revised interpretation as presented.

No additional concerns are noted.

Reviewer #4 (Public review):

Summary:

This work investigates whether a citation to a referee made by a paper is associated with a more positive evaluation by that referee for that paper. It provides evidence supporting this hypothesis. The work also investigates the role of self-citations by referees where the referee would ask authors to cite the referee's paper.

Strengths:

This is an important problem: referees for scientific papers must provide their impartial opinions rooted in core scientific principles. Any undue influence due to the role of citations breaks this requirement. This work studies the possible presence and extent of this.

The methods are solid and well done. The work uses a matched pair design which controls for article-level confounding and further investigates robustness to other potential confounds.

Weaknesses:

The authors have addressed most concerns in the initial review. The only remaining concern is the asymmetric reporting and highlighting of version 1 (null result) versus version 2 (rejecting null). For example the abstract says "We find that reviewers who were cited in the article under review were more likely to recommend approval, but only after the first version (odds ratio = 1.61; adjusted 99.4% CI: 1.16 to 2.23)" instead of a symmetric sentence "We find ... in version 1 and ... in version 2".

The latest version now includes the results for both versions.

Author response:

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

Reviewer #2 (Public review):

(1) Why would BPS not reduce RLS in WT cells? The authors could test whether OE of FIT2 reduces RLS in WT cells.  

Our data indicate that the iron regulon gets turned on naturally in old cells, presumably due to reduced iron sensing, limiting their lifespan. Although we haven’t tested it experimentally, BPS would also turn on the iron regulon presumably in wild type cells and therefore would have a redundant effect with the activation of the iron regulon that occurs naturally during normal aging. It may be interesting in the future to see if higher levels of BPS can shorten the lifespan of wildtype cells. Similarly, we would predict that overexpression of FIT2 may reduce the lifespan, as its deletion has been shown to extend RLS.  

(2) The authors should add a brief explanation for why the GDP1 promoter was chosen for Ssd1 OE.

We used the same promoter that was used to overexpress Ssd1 in all previous studies. This is now stated in the text along with the relevant citations. 

(3) On page 12, growth to saturation was described as glucose starvation. This is more accurately described as nutrient deprivation. Referring to it as glucose starvation is akin to CR, which growing to saturation is not. Ssd1 OE formed condensates upon saturation but not in CR. Why do the authors think Ssd1 OE did not form condensates upon CR?

Too mild a stress?

This is a fair comment, and we have now changed glucose starvation to nutrient deprivation, as it is more accurate. The effects of nutrient starvation are profound: the cell cycle stops, autophagy is induced, cells undergo the diauxic shift, metabolism changes. None of these changes occur during calorie restriction (0.05% glucose) such that it is not too surprising that Ssd1 does not form condensates during CR. We speculate that the stress is just too mild.   

(4) The authors conclude that the main mechanism for RLS extension in CR and Ssd1 OE is the inhibition of the iron regulon in aging cells. The data certainly supports this. However, this may be an overstatement as other mutations block CR, such as mutations that impair respiration. The authors do note that induction of the iron regulon in aging cells could be a response to impaired mitochondrial function. Thus, it seems that the main goal of CR and Ssd1 OE may be to restore mitochondrial function in aging cells, one way being inactivation of the iron regulon. A discussion of how other mutations impact CR would be of benefit.

While some labs have shown that respiration impacts CR, this is not the case in other studies. For example, an impactful paper by Kaeberlein et al., PLOS Genetics 2005 showed that CR does extend lifespan in respiratory deficient strains using many different strain backgrounds.

(5) The cell cycle regulation of Ssd1 OE condensates is very interesting. There does not appear to be literature linking Ssd1 with proteasome-dependent protein turnover. Many proteins involved in cell cycle regulation and genome stability are regulated through ubiquitination. It is not necessary to do anything here about it, but it would be interesting to address how Ssd1 condensates may be regulated with such precision.

we see no evidence of changes in Ssd1 protein intensity during the cell cycle. The difference therefore we speculate is at the post translational level rather than Ssd1 degradation and there are known cell cycle regulated phosphatase and kinase that regulates Ssd1 phosphorylation and condensation state whose timing of function match when the Ssd1 condensates appear and dissolve in the cell cycle. We have now discussed this and elude to it in the model. 

(6) While reading the draft, I kept asking myself what the relevance to human biology was. I was very impressed with the extensive literature review at the end of the discussion, going over how well conserved this strategy is in yeast with humans. I suggest referring to this earlier, perhaps even in the abstract. This would nail down how relevant this model is for understanding human longevity regulation.

Thank you, we have now mentioned in the abstract the relevance to human work. 

In conclusion, I enjoyed reading this manuscript, describing how Ssd1 OE and CR lead to RLS increases, using different mechanisms. However, since the 2 strategies appear to be using redundant mechanisms, I was surprised that synergism was not observed.

We thank the reviewer for their kind comment. We propose that Ssd1 overexpression impacts the levels of the iron regulon transcripts, which would be downstream of the point in the pathway that is affected by CR, i.e., nuclear localization of Aft1. The lack of synergy fits with this model, as Ssd1 overexpression cannot impact the iron regulon transcripts if they are not induced due to CR. We have now improved the model to make the impact of these different anti-aging interventions on activation of the iron regulon more clear.

Reviewer #3 (Public review):

My main concern is that the central reasoning of the paper-that Ssd1 overexpression and CR prevent the activation of the iron regulon-appears to be contradicted by previous findings, and the authors may actually be misrepresenting these studies, unless I am mistaken. In the manuscript, the authors state on two occasions:

"Intriguingly, transcripts that had altered abundance in CR vs control media and in SSD1 vs ssd1∆ yeast included the FIT1, FIT2, FIT3, and ARN1 genes of the iron regulon (8)"

"Ssd1 and CR both reduce the levels of mRNAs of genes within the iron regulon: FIT1, FIT2, FIT3 and ARN1 (8)"

However, reference (8) by Kaeberlein et al. actually says the opposite:

"Using RNA derived from three independent experiments, a total of 97 genes were observed to undergo a change in expression >1.5-fold in SSD1-V cells relative to ssd1d cells (supplemental Table 1 at http://www.genetics.org/supplemental/). Of these 97 genes, only 6 underwent similar transcriptional changes in calorically restricted cells (Table 2). This is only slightly greater than the number of genes expected to overlap between the SSD1-V and CR datasets by chance and is in contrast to the highly significant overlap in transcriptional changes observed between CR and HAP4 overexpression (Lin et al. 2002) or between CR and high external osmolarity (Kaeberlein et al. 2002). Intriguingly, of the 6 genes that show similar transcriptional changes in calorically restricted cells and SSD1-V cells, 4 are involved in ironsiderochrome transport: FIT1, FIT2, FIT3, and ARN1 (supplemental Table 1 at http://www.genetics.org/supplemental/)."

Although the phrasing might be ambiguous at first reading, this interpretation is confirmed upon reviewing Matt Kaeberlein's PhD thesis: https://dspace.mit.edu/handle/1721.1/8318 (page 264 and so on).

Moreover, consistent with this, activation of the iron regulon during calorie restriction (or the diauxic shift) has also been observed in two other articles:

https://doi.org/10.1016/S1016-8478(23)13999-9

https://doi.org/10.1074/jbc.M307447200

Taken together, these contradictory data might blur the proposed model and make it unclear how to reconcile the results.

We thank the reviewer for pointing this out. Upon further consideration, we have now removed all mention of this paper from our manuscript as it is irrelevant to our situation, because the mRNA abundance studies during CR or with and without Ssd1 were not performed in situations in which the iron regulon is even activated such as aging, so there would not be any opportunity to detect reduced transcript levels due to CR or Ssd1 presence. Also, none of these studies were performed with Ssd1 overexpression which is the situation we are examining.  Our data clearly show that Ssd1 overexpression and CR reduced / prevented, respectively, production of proteins from the iron regulon during aging.

We do not feel that the iron regulon being activated by nutrient depletion at the diauxic shift is a fair comparison to the situation in cells happily dividing during CR. The levels of nutrient deprivation used in those studies have profound effects including arresting cell growth, activating autophagy, altering metabolism. The levels of CR that we use (0.05% glucose) does not activate any of these changes nor the iron regulon in young cells or old cells (Fig. 4).  

Reviewer #1 (Recommendations for the authors):

(1) The role of Ssd1 condensate formation in mRNA sequestration and lifespan expansion remains unclear. Thus, the study involves two parts (Ssd1 condensate formation and lifespan expansion via limiting Fe2+ accumulation), which are poorly linked. The study will therefore benefit from further data linking the two aspects.

Future experiments are planned to determine what mRNAs reside in the age-induced Ssd1 overexpression condensates, to determine if they include the iron regulon transcripts. This will require us to optimize isolation of old cells and isolation of the Ssd1 condensates from them, and is beyond the scope of the present study.

(2) The beneficial effects of Ssd1 overexpression and calorie restriction (CR) on lifespan are epistatic, yet the claim that both experimental conditions act via the same pathway should be further documented. It is recommended to combine Ssd1 overexpression with a well-defined condition that expands lifespan through a mechanism not involving changes in Fe2+ levels. A further increase in lifespan upon combining such conditions would at least indirectly support the authors' claim.

We have more than epistatic evidence to indicate that Ssd1 overexpression and CR are in the same pathway. Ssd1 overexpression and CR result in failure to properly induce the iron regulon during aging and subsequent reduced levels of iron, resulting in lifespan extension, supporting that they act via the same pathway. We do appreciate the point though and epistasis analyses are on our list for future studies.

(3) It is highly recommended to analyze ssd1 knockout cells: Is the shortened lifespan caused by intracellular Fe2+ accumulation, as predicted by the model? Does the knockout lead to an overactivation of the iron regulon? Such analysis will also document the physiological relevance of authentic Ssd1 levels in controlling yeast lifespan. The authors could test this possibility by determining intracellular Fe2+ levels (as done in Figure 5) and testing whether the mutant cells are partially rescued by the presence of an iron chelator (as done in Figure 5C).

We don’t think the normal role of Ssd1 is to sequester the iron regulon mRNAs to prevent its activation, given that wild type yeast with endogenous Ssd1 activates the iron regulon during aging. Rather, the failure to activate the iron regulon during aging is unique to when Ssd1 is overexpressed not at endogenous Ssd1 levels. As such, it may not be the case that the short lifespan of ssd1 yeast is due to iron accumulation (if that happens); yeast lacking SSD1 also have cell wall biogenesis problems and the defects in cell wall biogenesis shorten the replicative lifespan (Molon et al., Biogerentology 2018  PMID 29189912). 

(4) Figure 4: The authors could not analyze the impact of Ssd1 overexpression on the localization of GFP-Aft1 due to synthetic sickness. This was not observed under calorie restriction (CR) conditions and is therefore unexpected. Why should Ssd1 overexpression and CR have such diverse impacts on cellular physiology when combined with GFP-Aft1? Isn`t that observation arguing against CR and increased Ssd1 levels acting through the same pathway? A further clarification of this point is necessary.

Without further experimentation, we can only speculate that cellular changes that are unique to overexpression of Ssd1 and not shared with CR cause a negative interaction with GFP-Aft1. Of note, Aft1 has functions in addition to its role in activating the iron regulon (aft1∆ strains have a growth defect independent from its role in iron regulon activation [27]) and we have shown previously that overexpressed Ssd1 has a reduction in global protein translation. Future experiments would be necessary to delineate the basis for this synthetic sickness.

(5) Lowering Fe2+ levels upon Ssd1 overexpression is predicted to reduce oxidative stress. It is suggested to determine ROS levels upon Ssd1 overexpression to bolster that point.

This is a great suggestion. The lowering of Fe2+ in the Ssd1 mutants is something that happens at the end of the lifespan and therefore we would need to do experiments to detect reduced ROS using a live dye on our microfluidics platform. We are not aware of any live fluorescent reporters of ROS.  

Reviewer #2 (Recommendations for the authors):

(1) Page 6, 7th line of Replicative lifespan analyses, there is a double bracket.

This has been corrected. Thank you

(2) Page 18, line 6 of "failure to activate..." section, "revered" should be replaced with "reversed".

This has been corrected. Thank you

(3) Page 23, fix writing on line 2 of "Effects of CR..." section.

This has been corrected. Thank you

(4) Page 24, Author contributions section, replace "performed devised" with "designed".

This has been corrected. Thank you

Reviewer #3 (Recommendations for the authors):

(1) Figure 3C: The panel legend is somewhat confusing due to the color scheme and the scattering of labels across panels. A more consistent labeling strategy would help readability.

We agree, and the labelling has now been improved. Thank you. 

(2) Figure 3D vs Figure 3B: it appears that Fit2 activation occurs substantially earlier than Aft1 translocation, which reduces the predictive value of Fit2 compared to Aft1. This is puzzling given that Fit2 is expected to be a direct target of Aft1. Could this discrepancy be related to the thresholding used for Fit2-mCherry display? The color scale in Figure 3D is also somewhat misleading, as most of the segments appear greenish. A continuous color gradient, perhaps restricted to the [10-120] interval, might give a clearer picture of iron regulon activation.

For the Aft1-mcherry experiment, we are only able to accurately annotate nuclear localization when Aft1 has been fully (or mostly) translocated into the nucleus from the cytoplasm such that this data is likely to be on the conservative side. However, activation of the iron regulon likely occurs as Aft1 is translocated into the nucleolus, so a minimal initial amount of Aft1 (for which we don’t have enough resolution in this system to detect) could be enough for FIT2 and ARN1 induction.  By contrast, the Fit2 and Arn1 signal is measuring increase over a background of nothing, so is very easy to detect even at low level induction. To allow the readers to see all our data without over thresholding, we prefer to present the induction of Fit2 and Arn1 at all intensity levels even the very low level induction (green).

(3) "In control strains, expression of Fit2 and Arn1 varied across the population, but generally increased with age": for the right panel, normalization might be more appropriate. What is the fold change in fluorescence during lifespan? Reporting ΔmCherry intensity alone does not provide a quantitative measure of induction.

We have changed the figure to show quantitation as fold change, as suggested.

(4) Figure 6 (model): The model figure is conceptually useful but not easy to follow in its current form; a revised schematic with a clearer depiction of the pathway activations at different replicative ages would be helpful.

We have changed the figure to make the model more clear, as suggested.

Author response:

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

Reviewer #1 (Public Review):

Summary:

Ravichandran et al investigate the regulatory panels that determine the polarization state of macrophages. They identify regulatory factors involved in M1 and M2 polarization states by using their network analysis pipeline. They demonstrate that a set of three regulatory factors (RFs) i.e., CEBPB, NFE2L2, and BCL3 can change macrophage polarization from the M1 state to the M2 state. They also show that siRNA-mediated knockdown of those 3-RF in THP1-derived M0 cells, in the presence of M1 stimulant increases the expression of M2 markers and showed decreased bactericidal effect. This study provides an elegant computational framework to explore the macrophage heterogeneity upon different external stimuli and adds an interesting approach to understanding the dynamics of macrophage phenotypes after pathogen challenge.

Strengths:

This study identified new regulatory factors involved in M1 to M2 macrophage polarization. The authors used their own network analysis pipeline to analyze the available datasets. The authors showed 13 different clusters of macrophages that encounter different external stimuli, which is interesting and could be translationally relevant as in physiological conditions after pathogen challenge, the body shows dynamic changes in different cytokines/chemokines that could lead to different polarization states of macrophages. The authors validated their primary computational findings with in vitro assays by knocking down the three regulatory factors-NCB.

We thank the reviewer for reading our manuscript and for the encouraging comments.

Weaknesses:

One weakness of the paper is the insufficient analysis performed on all the clusters. They used macrophages treated with 28 distinct stimuli, which included a very interesting combination of pro- and anti-inflammatory cytokines/factors that can be very important in the context of in vivo pathogen challenge, but they did not characterize the full spectrum of clusters. 

We have performed a functional enrichment analysis of all the clusters and added a section describing the results (Fig 1B). We believe this work will provide a basis for future experiments to characterize other clusters.

We have also performed a Principal Component Analysis (PCA) using hall mark genes of inflammation and the NCB panel alone to show the relative position of all clusters with respect to each other

Although they mentioned that their identified regulatory panels could determine the precise polarization state, they restricted their analysis to only the two well-established macrophage polarization states, M1 and M2. Analyzing the other states beyond M1 and M2 could substantially advance the field. They mentioned the regulatory factors involved in individual clusters but did not study the potential pathway involving the target genes of these regulatory factors, which can show the importance of different macrophage polarization states. Importantly, these findings were not validated in primary cells or using in vivo models.

We agree it would be useful to demonstrate the polarization switch in other systems as well. However, it is currently infeasible for us to perform these experiments. 

Reviewer #2 (Public Review):

Summary:

The authors of this manuscript address an important question regarding how macrophages respond to external stimuli to create different functional phenotypes, also known as macrophage polarization. Although this has been studied extensively, the authors argue that the transcription factors that mediate the change in state in response to a specific trigger remain unknown. They create a "master" human gene regulatory network and then analyze existing gene expression data consisting of PBMC-derived macrophage response to 28 stimuli, which they sort into thirteen different states defined by perturbed gene expression networks. They then identify the top transcription factors involved in each response that have the strongest predicted association with the perturbation patterns they identify. Finally, using S. aureus infection as one example of a stimulus that macrophages respond to, they infect THP-1 cells while perturbing regulatory factors that they have identified and show that these factors have a functional effect on the macrophage response.

Strengths:

The computational work done to create a "master" hGRN, response networks for each of the 28 stimuli studied, and the clustering of stimuli into 13 macrophage states is useful. The data generated will be a helpful resource for researchers who want to determine the regulatory factors involved in response to a particular stimulus and could serve as a hypothesis generator for future studies.

The streamlined system used here - macrophages in culture responding to a single stimulus - is useful for removing confounding factors and studying the elements involved in response to each stimulus.

The use of a functional study with S. aureus infection is helpful to provide proof of principle that the authors' computational analysis generates data that is testable and valid for in vitro analysis.

We thank the reviewer for reading our manuscript and for the encouraging comments

Weaknesses:

Although a streamlined system is helpful for interrogating responses to a stimulus without the confounding effects of other factors, the reality is that macrophages respond to these stimuli within a niche and while interacting with other cell types. The functional analysis shown is just the first step in testing a hypothesis generated from this data and should be followed with analysis in primary human cells or in an in vivo model system if possible.

It would be helpful for the authors to determine whether the effects they see in the THP-1 immortalized cell line are reproduced in another macrophage cell line, or ideally in PBMC-derived macrophages.

We agree; It would be useful in the future to demonstrate the polarization switch in other systems as well. We believe the results we provide here will inform future studies on other systems. 

The paper would benefit from an expanded explanation of the network mining approach used, as well as the cluster stability analysis and the Epitracer analysis. Although these approaches may be published elsewhere, readers with a non-computational background would benefit from additional descriptions.

We have elaborated on the network mining approach and added a schematic diagram (Fig S13) to describe the EpiTracer algorithm.

Although the authors identify 13 different polarization states, they return to the iM0/M1/M2 paradigm for their validation and functional assays. It would be useful to comment on the broader applications of a 13-state model.

We have included a new figure panel describing the functional enrichment analysis of all the clusters (Fig 1B) and added a section describing the results. We have also performed a Principal Component Analysis (PCA) using hallmark gene of inflammation and the NCB panel alone to show the relative position of all clusters with respect to each other. The PCA plot shows that C11(M1) and C3(M2) are roughly at two extreme ends, with other clusters between them, forming something resembling a punctuated continuum of states.

The relative contributions of each "switching factor" to the phenotype remain unclear, especially as knocking out each individual factor changes different aspects of the model (Fig. S5).

Fig S5 shows the effect on phenotype upon individual knockdown of the switching factors, from which we deduce that CEBPB has the largest contribution in determining the phenotype. However, we maintain that all three genes are necessary as a panel for M1/M2 switching. 

Reviewer #1 (Recommendations For The Authors):

The manuscript by Ravichandran et al describes the networks of genes that they named j"RF" associated with M1 to M2 polarization of macrophages by using their computational pipelines. They have shown 13 clusters of human macrophage polarization state by using an available database of different combinatorial treatments with cytokines, endotoxin, or growth factors, which is interesting and could be useful in the research field. However, there are a few comments which will help to understand the subject more precisely.

(1,2) The authors claimed to identify key regulatory factors involved in the human macrophage polarization from M1 to M2. However, recent advances suggest that macrophage polarization cannot be restricted to M1 and M2 only, which is also supported by the authors' data that shows 13 clusters of macrophages. However, they only focused on the difference between clusters 11 and 3 considering conventional M1 and M2. It will be more interesting to analyze the other clusters and how they relate to the established and simplistic M1 and M2 paradigms.

It will be interesting to know if they found any difference in the enriched pathways among these different clusters considering the exclusive regulatory factors and their targets.

We appreciate the point and have addressed it as follows. In the revised manuscript, we have discussed the clusters in detail and have provided the key regulatory factors (RF) combinations and target genes that define distinct macrophage population states (Please refer: Data file S2, S3). We have also discussed the associated immunological processes with each cluster, particularly in relation to the C11 and C3 clusters. We have added a new panel in Fig 1 to illustrate a heatmap indicating the enrichment of pathways relevant to inflammation in each of the clusters (Fig 1B).   Indeed, there is a substantial difference in the enrichment terms between the extreme ends (M1, M2) and significant differences in some of the pathways between clusters.   

(3) The authors have shown the involvement of NCB at 72h post LPS treatment. Are these RF involved in late response genes or act at the earlier time point of LPS treatment? Understanding the RF involvement in the dynamic response of macrophages to any stimulant will be important.

Using the data available for different time points (30 mins to 72 hours), we plotted the fold change (with respect to unstimulated cells) in M1 and M2 clusters for each of the NCB genes and observe clear divergence in the trend at 24 hours and have provided them as newly added (Supplementary Figure 9  A, B, C).

(4) The authors showed that the knockdown of RF- NCB can switch the M1 to M2. However, they showed a few conventional markers known to be M2 markers. What happens if NCB is overexpressed or knocked down in other treatment conditions/other clusters? Is the RF-NCB only involved in these two specific stimulations or their overexpression can promote M2 polarization in any given stimuli?

It is an interesting question but for practical reasons, experimental work was limited to M1 and M2 clusters as the aim was to establish proof of concept and could not be scaled up for all clusters, which would require a large amount of work and possibly a separate study.  We believe the description of the clusters that we have provided will enable the design of future experiments that will throw light on the significance of the intermediate clusters.  

(5) The authors have shown that knockdown of RF- NCB decreases pathogen clearance, but what are their altered functions? Are they more efficient in cellular debris clearance or resolution of inflammation? The authors can check the mRNA expression of markers/cytokines involved in those processes, in the NCB knockdown condition.

Indeed. Expression levels were measured for the following genes: CXCL2, IL1B, iNOS, SOCS3 (which are pro-inflammatory markers), as well as MRC1, ARG1, TGFB, IL10 (anti-inflammatory markers), as shown in Fig 4B.  

Minor comments:

(1, 2). How the authors evaluate the performance of their knowledge-based gene network. The authors should write the methods in detail, how they generated the simulated network, and evaluated the simulated dataset.

Gene network construction and module detection have many tools available. The authors need to mention which one they used. The authors should show whether their findings are consistent with at least another two module-detection methods (eg; "RedeR") to strengthen their claim.

We have added a schematic figure (Supplementary Fig S11) and detailed description of network construction and mining in the Methods section, as follows: We have reconstructed a comprehensive knowledge-based human Gene Regulatory Network (hGRN), which consists of Regulatory Factors (RF) to Target Gene (TG) and RF to RF interactions. To achieve this, we curated experimentally determined regulatory interactions (RF-TG, RF-RF) associated with human regulatory factors (Wingender et al., 2013). These interactions were sourced from several resources, including: (a) literature-curated resources like the Human Transcriptional Regulation Interactions database (HTRIdb) (Bovolenta et al., 2012), Regulatory Network Repository (RegNetwork) (Liu et al., 2015), Transcriptional Regulatory Relationships Unraveled by Sentence-based Text-mining (TRRUST) (Han et al., 2015), and the TRANSFAC resource from Harmonizome (Rouillard et al., 2016);  (b) ChEA3, which contains ChIP-seq determined interactions (Keenan et al., 2019); and (c) high-confidence protein-protein binding interactions (RF-RF) from the human protein-protein interaction network-2 (hPPiN2) (Ravichandran et al., 2021). As a result, our hGRN comprises 27,702 nodes and 890,991 interactions.  It is important to note that none of the edges/interactions in the hGRN are data-driven. We utilized this extensive hGRN, which encompasses the experimentally determined interactions/edges, to infer stimulant-specific hGRNs and top paths using our in-house network mining algorithm, ResponseNet. We have previously demonstrated that ResponseNet, which utilizes a knowledge-based network and a sensitive interrogation algorithm, outperformed data-driven network inference methods in capturing biologically relevant processes and genes, whose validation is reported earlier (Ravichandran and Chandra, 2019; Sambaturu et al., 2021).

We utilized our in-house response network approach to identify the stimulant-specific top active and repressed perturbations (Ravichandran and Chandra, 2019; Sambaturu et al., 2021). This is clearly described in the revised manuscript. To summarize, we generated stimulant-specific Gene Regulatory Networks (GRNs) by applying weights to the master human Gene Regulatory Network (hGRN) based on differential transcriptomic responses to stimulants (i.e., comparing stimulant-treated conditions to baseline). We then produced individually weighted networks for each stimulant and implemented a refined network mining technique to extract the most significant pathways. Furthermore, we have previously conducted a systematic comparison of our network mining strategy with other data-driven module detection methods, including jActiveModules (Ideker et al, 2002), WGCNA (Langfelder et al, 2008), and ARACNE (Margolin et al, 2006). Our findings demonstrated that our approach outperformed conventional data-driven network inference methods in capturing the biologically pertinent processes and genes (Ravichandran and Chandra, 2019). Since we have experimentally validated what we predicted from the network analysis, we do not see a need for performing the computational analysis with another algorithm. Moreover, different network analyses are based on different aspects of identifying functionally relevant genes or subnetworks. While each of them output useful information, given the scale of the network and the number of different biologically significant subnetworks and genes that could be present in an unbiased network such as what we have used, the output from different methods need not agree with each other as they may capture different aspects all together and hence is not guaranteed to be informative.  

(3) Representation of Fig 2B is difficult to understand the authors' interpretation of 'the 3-RF combination has 1293 targets, 359 covering about 53% of the top-perturbed network' for general readers. If the authors can simplify the interpretation will be helpful for the readers.

This is replaced with clearer figures in the revised manuscript (Figure 2A, 2B), and the associated text is also rephrased for clarity.

Reviewer #2 (Recommendations For The Authors):

Major comments:

(1) It would be helpful for the authors to determine whether the effects they see in the THP-1 immortalized cell line are reproduced in another macrophage cell line, or ideally in PBMC-derived macrophages if this is feasible. If using PBMC- or bone marrow-derived macrophages is beyond the scope of what the authors can reasonably perform, they could consider using another macrophage cell line such as RAW 264.7 cells, which would also provide orthogonal validation from a mouse model.

At this point of time, it is unfortunately infeasible for us to perform these experiments, due to resource limitation.  Moreover, it would require a lot of time. We hope that our work provides pointers for anyone working on mouse models or other model systems to design their studies on regulatory controls and the aspect of generalizability of our findings in Thp-1 cell lines to other systems will eventually emerge.

(2) It would be helpful for the authors to provide an expanded explanation of the network mining approach used, as well as the cluster stability analysis and the Epitracer analysis. Although these approaches may be published elsewhere, readers with a non-computational background would benefit from additional descriptions. A schematic figure would also be helpful to clarify their approach.

We have added a new schematic diagram in Supplementary figures (S13) and a detailed text in the Methods section describing the network mining analysis and epitracer identification in the revised manuscript. 

(3) It would be helpful for the authors to comment on whether the thirteen polarization states that they identify align with other analyses that have been performed using data collected from stimulated macrophages, or whether this is a novel finding, especially as the original paper from which the primary data are derived identified 9 clusters. More broadly, since the authors eventually return to the M1-M2 paradigm, it is unclear whether there is any functional support for a 13-state model - it is also possible that macrophages exist along a continuum of stimulation states rather than in discrete clusters. This at least merits further discussion, which could focus on different axes of polarization as discussed and shown in the original paper.

As described in the manuscript, Clustering based on the differential transcriptome profile of RF-set1, which contains 265 transcription factors (TFs), in response to 28 stimulants, resulted in 13 distinct clusters. The cluster member associations inferred from RF-set1 were similar in number and pattern to those inferred from the entire differential transcriptome (n=12,164; Fig. S2, cophenetic coefficient = 0.68; p-value = 1.25e−51). Furthermore, the inferred cluster pattern largely matched the clustering pattern previously described for the same dataset  (Xue et al., 2014).  Our contribution: The pattern we observed from the top-ranked epicenters in each cluster suggests that a subset of differentially expressed genes (DEGs) present in our top networks is sufficient for achieving differentiation. Our gene-regulatory models suggest that saturated (SA and PA) and unsaturated (LA, LiA, and OA) fatty acids, which were previously grouped together, mediate distinct modes of resolution and are now separated into two sub-branches. Similarly, the effects of IFNγ and sLPS, previously combined, are now distinctly resolved, aligning with known regulatory differences (Hoeksema et al., 2015; Kang et al., 2019). 

The principal takeaway from this analysis is not the exact number of clusters but rather the molecular basis it provides for the differentiation of functional states, with M1 and M2 representing two ends of the spectrum. Several other states are dispersed within the polarization spectrum, which we describe as a punctuated continuum. For our switching studies, we focused on clusters C11 (M1-like) and C2 (M2-like) due to their established functional relevance. However, future studies are required to explore the functional relevance of other clusters. We have added a discussion on this aspect as suggested.

(4) It would be helpful to define the contribution of each component of the NCB group to M1 polarization.

We assessed the impact of CEBPB, NFE2L2, and BCL3 on C2 (M1-like) polarization states by quantifying the expression levels of M1 and M2 markers. Our findings indicate that knocking down CEBPB led to a significant downregulation in the expression of M1 markers and an increase in M2 marker expression. In contrast, NFE2L2 and BCL3 knockdown resulted in decreased expression of M1 markers without a corresponding significant increase in M2 markers. These results suggest that CEBPB is crucial for M1 to the M2 transition. We have added a note on pg 22 to emphasize this better.

(5) NRF2, CEBPb, and BCL3 all have well-described roles in macrophage polarization. To add clarity to their discussion, the authors should cite relevant literature (eg PMIDs 15465827, 27211851, and others) and discuss how their findings extend what is currently known about the contribution of these individual proteins to macrophage responses.

The role of NFE2L2, CEBPB and BCL3 in macrophage polarization and state transition are described in the discussion section. The PMIDs mentioned by the reviewer are added as well. 

(6) The effect size of NCB knockdown in the in vitro Staph aureus model shown in 4C is fairly small - bacterial killing assays typically require at least a log of difference to demonstrate a convincing effect. It would be helpful for the authors to include a positive control for this experiment (for example, STAT4) to frame the magnitude of their effect.

We thank the reviewer for the comment, however, we would like to point out that the difference in CFU plotted in log₁₀ scale, as per common practice. The CFUs are therefore almost halved due to the knockdown in absolute scale and reproduced multiple times with statistically significant results (p-value <0.01). We feel it is sufficient to demonstrate that the NCB geneset by themselves bring out a change in polarization and hence the killing effect. We have used STAT4 as a control for marker measurements as shown in Fig 3C. While carrying out CFU with siSTAT4 may add additional information, we have proceeded to perform the infection experiments with and without the NCB knockdown as that remains the main focus of the study. 

Minor recommendations:

(1) Is there a difference between the data represented in Figure 1A-B and Figure S1? If this is the same data, there is no need to repeat it, and Figure 1 could be composed only of the current panels C and D.

We have removed Figure1 A and B as it illustrates the same point as Figure S1. We have retained Figures C and D and renamed them as new Figure 1A and C. In addition, we have added a new panel Fig 1B (in response to earlier points). 

(2) Could Figure 2B be represented in a different way? The circles do not contain any readable information about the genes, and it may be less visually overwhelming to represent this with just the large and small triangles. Perhaps the individual genes represented by the circles could be listed in a supplemental table or Excel file.

We have provided a new Figure 2 A and B panels for the M1 and M2 clusters respectively, which has only the barcode genes along with a functional annotation. The full network is already provided in supplementary data. 

(3) When indicating the N for all experiments performed in the figure legends, the authors should indicate whether these were technical or biological replicates.

We appreciate the reviewers for the suggestion. We have indicated what N is for all figure legends.

(4) Fig 3B: the y-axis is confusing - it appears that normalization is actually to the untreated cells.

Yes indeed. The normalization is with respect to the untreated cells as per standard practice. We have indicated this clearly in the legend.

(5) The 72-hour time point in Fig S8 shows unexpected results. Could the authors explain or propose a hypothesis for why CXCL2 and IL1b abruptly decrease while iNOS and MRC1 abruptly increase?

The purpose of the mentioned experiment was to standardize the time point of M1 polarization post S. aureus  infection. In this regard,  we profiled the expression levels of markers at various time points. We chose to study the 24 hour time point for all the future experiments based on the significant upregulation of NCB seen in the macrophages.  We believe that the 72 hour time point may show effects that are different since the initial immune response would have waned leading to differences in cytokine dynamics. However, as this is not the focus of our study, we are not discussing this aspect further.

Author response:

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

Reviewer #1 (Public Review):

Summary:

Crohn's disease is a prevalent inflammatory bowel disease that often results in patient relapse post anti-TNF blockades. This study employs a multifaceted approach utilizing single-cell RNA sequencing, flow cytometry, and histological analyses to elucidate the cellular alterations in pediatric Crohn's disease patients pre and post-anti-TNF treatment and comparing them with non-inflamed pediatric controls. Utilizing an innovative clustering approach, the research distinguishes distinct cellular states that signify the disease's progression and response to treatment. Notably, the study suggests that the anti-TNF treatment pushes pediatric patients towards a cellular state resembling adult patients with persistent relapses. This study's depth offers a nuanced understanding of cell states in CD progression that might forecast the disease trajectory and therapy response.

Robust Data Integration: The authors adeptly integrate diverse data types: scRNA-seq, histological images, flow cytometry, and clinical metadata, providing a holistic view of the disease mechanism and response to treatment.

Novel Clustering Approach: The introduction and utilization of ARBOL, a tiered clustering approach, enhances the granularity and reliability of cell type identification from scRNA-seq data.

Clinical Relevance: By associating scRNA-seq findings with clinical metadata, the study offers potentially significant insights into the trajectory of disease severity and anti-TNF response; which might help with the personalized treatment regimens.

Treatment Dynamics: The transition of the pediatric cellular ecosystem towards an adult, more treatment-refractory state upon anti-TNF treatment is a significant finding. It would be beneficial to probe deeper into the temporal dynamics and the mechanisms underlying this transition.

Comparative Analysis with Adult CD: The positioning of on-treatment biopsies between treatment-naïve pediCD and on-treatment adult CD is intriguing. A more in-depth exploration comparing pediatric and adult cellular ecosystems could provide valuable insights into disease evolution.

Areas of improvement:

(1) The legends accompanying the figures are quite concise. It would be beneficial to provide a more detailed description within the legends, incorporating specifics about the experiments conducted and a clearer representation of the data points. 

We agree that it is beneficial to have descriptive figure legends that balance elements of experimental design, methodology, and statistical analyses employed in order to have a clear understanding throughout the manuscript. We have gone through and clarified areas throughout.  

(2) Statistical significance is missing from Fig. 1c WBC count plot, Fig. 2 b-e panels. Please provide it even if it's not significant. Also, the legend should have the details of stat test used.

We have now added details of statistical significance data in the Figure 1 legends. Please note that Mann-Whitney U-test was used for clinical categorical data.

(3) In the study, the NOA group is characterized by patients who, after thorough clinical evaluations, were deemed to exhibit milder symptoms, negating the need for anti-TNF prescriptions. This mild nature could potentially align the NOA group closer to FGID-a condition intrinsically defined by its low to non-inflammatory characteristics. Such an alignment sparks curiosity: is there a marked correlation between these two groups? A preliminary observation suggesting such a relationship can be spotted in Figure 6, particularly panels A and B. Given the prevalence of FGID among the pediatric population, it might be prudent for the authors to delve deeper into this potential overlap, as insights gained from mild-CD cases could provide valuable information for managing FGID.

Thank you for this insightful point. On histopathology and endoscopy, the NOA exhibited microscopic and macroscopic inflammation which landed these patients with the CD diagnosis, albeit mild on both micro and macro accounts. By contrast, the FGID group by definition will not have inflammation of microscopic and macroscopic evaluation. There is great interest in the field of adult and pediatric gastroenterology to understand why patients develop symptoms without evidence of inflammation. However, in 2023 the diagnostic tools of endoscopy with biopsy and histopathology is not sensitive enough to detect transcript level inflammation, positioning single-cell technology to be able to reveal further information in both disease processes.

Based on the reviewer’s suggestions, we have calculated a heatmap of overlapping NOA and FGID cell states along the Figure 6a joint-PC1, showing where NOA CD patients and FGID patients overlap in terms of cell states. This is displayed in Supplemental Figure 15d. This revealed a set of T, Myeloid, and Epithelial cell states that were most important in describing variance along the FGID-CD axis, allowing us to hone in on similarities at the boundary between FGID and CD. By comparing the joint cell states with CD atlas curated cluster names, we identified CCR7-expressing T cell states and GSTA2-expressing epithelial states associated with this overlap. 

(4) Furthermore, Figure 7 employs multi-dimensional immunofluorescence to compare CD, encompassing all its subtypes, with FGID. If the data permits, subdividing CD into PR, FR, and NOA for this comparison could offer a more nuanced understanding of the disease spectrum. Such a granular perspective is invaluable for clinical assessments. The key question then remains: do the sample categorizations for the immunofluorescence study accommodate this proposed stratification?

Thank you for the thoughtful discussion. We agree that stratifying Crohn’s disease by PR, FR, and NOA would provide valuable clinical insight. Unfortunately our multiplex IF cohort was designed to maximize overall CD versus FGID comparisons and does not contain enough samples in patient subgroups to power such an analysis. We have highlighted this limitation in the text.  

(5)The study's most captivating revelation is the proximity of anti-TNF-treated pediatric CD (pediCD) biopsies to adult treatment-refractory CD. Such an observation naturally raises the question: How does this alignment compare to a standard adult colon, and what proportion of this similarity is genuinely disease-specific versus reflective of an adult state? To what degree does the similarity highlight disease-specific traits?

Delving deeper, it will be of interest to see whether anti-TNF treatment is nudging the transcriptional state of the cells towards a more mature adult stage or veering them into a treatment-resistant trajectory. If anti-TNF therapy is indeed steering cells toward a more adult-like state, it might signify a natural maturation process; however, if it's directing them toward a treatment-refractory state, the long-term therapeutic strategies for pediatric patients might need reconsideration.

Thank you to the reviewer for another insightful point. We agree that age-matched samples are critical to evaluate disease cell states and hence we have age-matched controls in our pediatric cohort. Our timeline of follow-up only spans 3 years and patients remain in the pediatric age range at times of follow-up endoscopy and biopsy and would not be reflective of an adult GI state. We believe that the cellular behavior from naïve to treatment biopsy to on treatment biopsy is reflective of disease state rather than movement towards and adult-like state. We would also like to point out that pediatric onset IBD (Crohn’s and ulcerative colitis) traditionally has been harder to treat and presents with more extensive disease state (PMID: 22643596) and the ability to detect need for therapy escalation/change would be an invaluable tool for clinicians.  

We share the reviewer’s interest in disentangling a natural maturation process from disease and treatment-specific changes. Because the patients who were not given treatment did not move towards the adult-like phenotype, it could point to a push towards a treatment-resistant trajectory. To further support these findings, we generated a new disease-pseudotime figure Supplemental Figure 17, using cross-validation methods and the TradeSeq package. This figure was designed to track how each pediatric sample shifts from the treatment-naïve state through antiTNF therapy and to test the robustness of these shifts across samples. The new visualizations show patterns that do not recapitulate natural aging processes but rather shifts across all cell types associated with antiTNF treatment.

Reviewer #2 (Public Review):

Summary:

Through this study, the authors combine a number of innovative technologies including scRNAseq to provide insight into Crohn's disease. Importantly samples from pediatric patients are included. The authors develop a principled and unbiased tiered clustering approach, termed ARBOL. Through high-resolution scRNAseq analysis the authors identify differences in cell subsets and states during pediCD relative to FGID. The authors provide histology data demonstrating T cell localisation within the epithelium. Importantly, the authors find anti-TNF treatment pushes the pediatric cellular ecosystem toward an adult state.

Strengths:

This study is well presented. The introduction clearly explains the important knowledge gaps in the field, the importance of this research, the samples that are used, and study design.

The results clearly explain the data, without overstating any findings. The data is well presented. The discussion expands on key findings and any limitations to the study are clearly explained.

I think the biological findings from, and bioinformatic approach used in this study, will be of interest to many and significantly add to the field.

Weaknesses:

(1) The ARBOL approach for iterative tiered clustering on a specific disease condition was demonstrated to work very well on the datasets generated in this study where there were no obvious batch effects across patients. What if strong batch effects are present across donors where PCA fails to mitigate such effects? Are there any batch correction tools implemented in ARBOL for such cases?

We thank the reviewer for their insightful point, the full extent to which ARBOL can address batch effects requires further study. To this end we integrated Harmony into the ARBOL architecture and used it in the paper to integrate a previous study with the data presented (Figure 8). We have added to ARBOL’s github README how to use Harmony with the automated clustering method. With ARBOL, as well as traditional clustering methods, batch effects can cause artifactual clustering at any tier of clustering. Due to iteration, this can cause batch effects to present themselves in a single round of clustering, followed by further rounds of clustering that appear highly similar within each batch subset. Harmony addresses this issue, removing these batch-related clustering rounds. The later arrangement of fine-grained clusters using the bottom-up approach can use the batch-corrected latent space to calculate relationships between cell states, removing the effects from both sides of the algorithm. As stated, the extent to which ARBOL can be used to systematically address these batch effects requires further research, but the algorithmic architecture of ARBOL is well suited to address these effects.

(2) The authors mentioned that the clustering tree from the recursive sub-clustering contained too much noise, and they therefore used another approach to build a hierarchical clustering tree for the bottom-level clusters based on unified gene space. But in general, how consistent are these two trees?

Thank you for this thoughtful question. The two tree methodologies are not consistent due to their algorithmic differences, but both are important for several reasons: 

(1) The clustering tree is top-down, meaning low resolution lineage-related clusters are calculated first. Doublets and quality differences can cause very small clusters of different lineages (endothelial vs fibroblast) to fall under the incorrect lineage at first in the sub clustering tree, but these are recaptured during further sub clustering rounds, and then disentangled by the cluster-centroid tree.

(2) The hierarchical tree is a rose tree, meaning each branching point can contain several daughter branches, while taxonomies based on distances between species (or cell types in this case) are binary trees with only 2 branches per branching point, because distances between each cluster are unique. Because this taxonomy, or bottom-up, is different from the top-down approach, it is useful to then look at how these bottom-level clusters are similar. To that end, we performed pair-wise differential expression between all end clusters and clustered based on those genes. 

(3) Calculation of a binary tree represents a quantitative basis for comparing the transcriptomic distance between clusters as opposed to relying on distances calculated within a heuristic manifold such as UMAP or algorithmic similarity space such as cluster definitions based on KNN graphs.

In practice, this dual view rescues small clusters that may have been mis-grouped by technical artifacts and gives a quantitative distance based hierarchy that can be compared across metadata covariates.

Author response:

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

Reviewer #1 (Public review): 

Summary:

In their previous publication (Dong et al. Cell Reports 2024), the authors showed that citalopram treatment resulted in reduced tumor size by binding to the E380 site of GLUT1 and inhibiting the glycolytic metabolism of HCC cells, instead of the classical citalopram receptor. Given that C5aR1 was also identified as the potential receptor of citalopram in the previous report, the authors focused on exploring the potential of the immune-dependent anti-tumor effect of citalopram via C5aR1. C5aR1 was found to be expressed on tumor-associated macrophages (TAMs) and citalopram administration showed potential to improve the stability of C5aR1 in vitro. Through macrophage depletion and adoptive transfer approaches in HCC mouse models, the data demonstrated the potential importance of C5aR1-expressing macrophage in the anti-tumor effect of citalopram in vivo. Mechanistically, their in vitro data suggested that citalopram may regulate the phagocytosis potential and polarization of macrophages through C5aR1. Next, they tried to investigate the direct link between citalopram and CD8+T cells by including an additional MASH-associated HCC mouse model. Their data suggest that citalopram may upregulate the glycolytic metabolism of CD8+T cells, probability via GLUT3 but not GLUT1-mediated glucose uptake. Lastly, as the systemic 5-HT level is down-regulated by citalopram, the authors analyzed the association between a low 5-HT and a superior CD8+T cell function against a tumor. Although the data is informative, the rationale for working on additional mechanisms and logical links among different parts is not clear. In addition, some of the conclusion is also not fully supported by the current data. 

We thank the reviewer for their comprehensive summary of our study and appreciate the valuable feedback. We have made improvements based on these comments, and a detailed response addressing each point is presented below.

Strengths: 

The idea of repurposing clinical-in-used drugs showed great potential for immediate clinical translation. The data here suggested that the anti-depression drug, citalopram displayed an immune regulatory role on TAM via a new target C5aR1 in HCC.

We thank the reviewer for recognizing the strengths of our study.

Weaknesses: 

(1) The authors concluded that citalopram had a 'potential immune-dependent effect' based on the tumor weight difference between Rag-/- and C57 mice in Figure 1. However, tumor weight differences may also be attributed to a non-immune regulatory pathway. In addition, how do the authors calculate relative tumor weight? What is the rationale for using relative one but not absolute tumor weight to reflect the anti-tumor effect? 

We appreciate your insights into the potential contributions of non-immune regulatory pathways to the observed tumor weight differences between Rag1^-/-and wild type C57BL/6 mice. Indeed, the anti-tumor effects of citalopram involve non-immune mechanisms. Previously, we have demonstrated the direct effects of citalopram on cancer cell proliferation, apoptosis, and metabolic processes (PMID: 39388353). In this study, we focused on immune-dependent mechanisms, utilizing Rag1^-/- mice to investigate a potential immune-mediated effect. The relative tumor weight was calculated by assigning an arbitrary value of 1 to the Rag1^-/- mice in the DMSO treatment group, with all other tumor weights expressed relative to this baseline. As suggested, we have included absolute tumor weight data in the revised Figure 1B, 1E, 1F, and 3B.

(2) The authors used shSlc6a4 tumor cell lines to demonstrate that citalopram's effects are independent of the conventional SERT receptor (Figure 1C-F). However, this does not entirely exclude the possibility that SERT may still play a role in this context, as it can be expressed in other cells within the tumor microenvironment. What is the expression profiling of Slc6a4 in the HCC tumor microenvironment? In addition, in Figure 1F, the tumor growth of shSlc6a4 in C57 mice displayed a decreased trend, suggesting a possible role of Slc6a4. 

As suggested, we probed the expression pattern of SERT in HCC and its tumor microenvironment. Using a single cell sequencing dataset of HCC (GSE125449), we revealed that SERT is also expressed by T cells, tumor-associated endothelial cells, and cancer-associated fibroblasts (see revised Figure S2G). Therefore, we cannot fully rule out the possibility that citalopram may influence these cellular components within the TME and contribute to its therapeutic effects. In the revised manuscript, we have included and discussed this result. In Figure 1F, SERT knockdown led to a 9% reduction in tumor growth, however, this difference was not statistically significant (0.619 ± 0.099 g vs. 0.594 ± 0.129 g; p = 0.75).

(3) Why did the authors choose to study phagocytosis in Figures 3G-H? As an important player, TAM regulates tumor growth via various mechanisms. 

We choose to investigate phagocytosis because citalopram targets C5aR1-expressing TAM. C5aR1 is a receptor for the complement component C5a, which plays a crucial role in mediating the phagocytosis process in macrophages. In the revised manuscript, we have highlighted this rationale.

(4) The information on unchanged deposition of C5a has been mentioned in this manuscript (Figures 3D and 3F), the authors should explain further in the manuscript, for example, C5a could bind to receptors other than C5aR1 and/or C5a bind to C5aR1 by different docking anchors compared with citalopram.

Thank you for your insightful comment. In Figure 3D, tumor growth was attenuated in C5ar1^-/- recipients compared with C5ar1^-/- recipients, whereas C5a deposition remained unchanged. This suggests that while C5a is still present, its interaction with C5aR1 is critical for influencing tumor growth dynamics. In Figure 3F, C5a deposition was not affected by citalopram treatment. Indeed, docking analysis and DARTS assay revealed that citalopram binds to the D282 site of C5aR1. Previous report has shown that mutations on E199 and D282 reduce C5a binding affinity to C5aR1 (PMID: 37169960). Therefore, the impact of citalopram is primarily on C5a/C5aR1 interactions and downstream signaling pathways, rather than on altering C5a levels. In the revised manuscript, we have included this interpretation.

(5) Figure 3I-M - the flow cytometry data suggested that citalopram treatment altered the proportions of total TAM, M1 and M2 subsets, CD4⁺ and CD8⁺T cells, DCs, and B cells. Why does the author conclude that the enhanced phagocytosis of TAM was one of the major mechanisms of citalopram? As the overall TAM number was regulated, the contribution of phagocytosis to tumor growth may be limited. 

We thank the reviewer’s valuable input. Indeed, recent studies have demonstrated that targeting C5aR1⁺ TAMs can induce many anti-tumor effects, such as macrophage polarization and CD8⁺ T cell infiltration (PMID: 30300579, PMID: 38331868, and PMID: 38098230). In the revised manuscript, we have clarified our conclusion to better articulate the relationship between citalopram treatment, TAM populations, and their phagocytic activity, with particular emphasis on the role of CD8⁺ T cells. For macrophage phagocytosis, one possible explanation is that citalopram targets C5aR1 to enhance macrophage phagocytosis and subsequent antigen presentation and/or cytokine production, which promotes T cell recruitment and activity as well as modulate other aspects of tumor immunity. Given that the anti-tumor effects of citalopram are largely dependent on CD8⁺ T cells, we conclude that CD8⁺ T cells are essential for the effector mechanisms of citalopram.

(6) Figure 4 - what is the rationale for using the MASH-associated HCC mouse model to study metabolic regulation in CD8⁺ T cells? The tumor microenvironment and tumor growth would be quite different. In addition, how does this part link up with the mechanisms related to C5aR1 and TAM? The authors also brought GLUT1 back in the last part and focused on CD8⁺ T cell metabolism, which was totally separated from previous data. 

We chose the MASH-associated HCC mouse model because it closely mimics the etiology of metabolic-associated fatty liver disease (MAFLD), which is a significant contributor to the development of cirrhosis and HCC. In addition to the MASH-associated HCC mouse model, the study also incorporated the orthotopic Hepa1-6 tumor model. In our previous publication (Dong et al., Cell Reports 2024), we employed both of these HCC models. Therefore, we utilized the same two mouse models in this study. The inclusion of CD8⁺ T cells in our study is based on the understanding that citalopram targets GLUT1, which plays a crucial role in glucose uptake (PMID: 39388353). CD8⁺T cell function is heavily reliant on glycolytic metabolism, making it essential to investigate how citalopram’s effects on GLUT1 influence the metabolic pathways and functionality of these immune cells. In this study, we identified that the primary glucose transporter in CD8⁺ T cells is GLUT3, rather than GLUT1. The data presented in Figure 4 aim to illustrate the additional effect of citalopram on peripheral 5-HT levels, which, in turn, influences CD8⁺ T cell functionality. By linking these findings, we clarify how citalopram impacts both TAMs and CD8⁺ T cells. CD8⁺ T cells can be influenced by citalopram through various mechanisms, including TAM-dependent mechanisms, reduced systemic serum 5-HT concentrations, and unidentified direct effects. In the revised manuscript, we have enhanced the background information to avoid any gaps.

(7) Figure 5, the authors illustrated their mechanism that citalopram regulates CD8⁺ T cell anti-tumor immunity through proinflammatory TAM with no experimental evidence. Using only CD206 and MHCII to represent TAM subsets obviously is not sufficient. 

Thank you for your valuable comments. As noted by the reviewer, TAMs can influence CD8⁺ T cell anti-tumor immunity through various mechanisms. In this study, we focused on elucidating the impact of citalopram on pro-inflammatory TAMs, which in turn affect CD8⁺ T cell anti-tumor immunity and ultimately influence tumor outcomes. Therefore, in the mechanistic diagram, we highlighted the effect of citalopram on pro-inflammatory TAMs, while the causal relationship between TAMs and CD8⁺ T cell anti-tumor immunity was indicated with a dotted line due to the limited evidence presented in this study. Additionally, we have expanded our discussion on how citalopram regulates CD8⁺ T cell anti-tumor immunity through pro-inflammatory TAMs.

For the analysis of TAMs, we initially sorted CD45⁺F4/80⁺CD11b⁺ cells and assessed M1/M2 polarization by measuring CD206 and MHCII expression. As an added strength, we isolated TAMs from the orthotopic GLUT1^KD Hepa1-6 model using CD11b microbeads and conducted real-time qPCR analysis of M1-oriented (Il6, Ifnb1, and Nos2) and M2-oriented (Mrc1, Il10, and Arg1) markers. Consistent with our flow cytometry data, the qPCR results confirmed that citalopram induces a pro-inflammatory TAM phenotype (revised Figure S9A).

Reviewer #2 (Public review): Summary: 

Dong et al. present a thorough investigation into the potential of repurposing citalopram, an SSRI, for hepatocellular carcinoma (HCC) therapy. The study highlights the dual mechanisms by which citalopram exerts anti-tumor effects: reprogramming tumor-associated macrophages (TAMs) toward an anti-tumor phenotype via C5aR1 modulation and suppressing cancer cell metabolism through GLUT1 inhibition while enhancing CD8+ T cell activation. The findings emphasize the potential of drug repurposing strategies and position C5aR1 as a promising immunotherapeutic target. However, certain aspects of experimental design and clinical relevance could be further developed to strengthen the study's impact. 

We thank the reviewer’s thoughtful review and constructive feedback. As suggested, we have made improvements based on the feedback provided.

Strength: 

It provides detailed evidence of citalopram's non-canonical action on C5aR1, demonstrating its ability to modulate macrophage behavior and enhance CD8+ T cell cytotoxicity. The use of DARTS assays, in silico docking, and gene signature network analyses offers robust validation of drug-target interactions. Additionally, the dual focus on immune cell reprogramming and metabolic suppression presents a thorough strategy for HCC therapy. By emphasizing the potential for existing drugs like citalopram to be repurposed, the study also underscores the feasibility of translational applications. 

We sincerely appreciate the reviewer’s recognition of the detailed evidence supporting citalopram’s non-canonical action on C5aR1, along with the innovative methodologies employed and the promising potential for repurposing existing drugs in HCC therapy.

Major weaknesses/suggestions: 

The dataset and signature database used for GSEA analyses are not clearly specified, limiting reproducibility. The manuscript does not fully explore the potential promiscuity of citalopram's interactions across GLUT1, C5aR1, and SERT1, which could provide a deeper understanding of binding selectivity. The absence of GLUT1 knockdown or knockout experiments in macrophages prevents a complete assessment of GLUT1's role in macrophage versus tumor cell metabolism. Furthermore, there is minimal discussion of clinical data on SSRI use in HCC patients. Incorporating survival outcomes based on SSRI treatment could strengthen the study's translational relevance. 

By addressing these limitations, the manuscript could make an even stronger contribution to the fields of cancer immunotherapy and drug repurposing. 

We appreciate the reviewer’s valuable suggestions. As suggested, we have included the following revisions:

(a) GSEA analyses: For GSEA analyses, we conducted RNA sequencing (RNA-seq) analysis on HCC-LM3 cells treated with citalopram or fluvoxamine, which led to the identification of 114 differentially expressed genes (DEGs; 80 co-upregulated and 34 co-downregulated), as reported previously (PMID: 39388353). These DEGs were then utilized to create an SSRI-related gene signature. Subsequently, we analyzed RNA-seq data from liver HCC (LIHC) samples in The Cancer Genome Atlas (TCGA) cohort, comprising 371 samples, categorizing them into high and low expression groups based on the median expression levels of each candidate target gene (such as C5AR1). Finally, we performed GSEA on the grouped samples (C5AR1-high versus C5AR1-low) using the SSRI-related gene signature. In the revised manuscript, we have included this information in the “Materials and Methods” section.

(b) Exploration of binding selectivity: We acknowledge the importance of exploring the potential promiscuity of citalopram’s interactions across GLUT1, C5aR1, and SERT1. While we cannot provide further experimental data to support this aspect, we have included the following points in the revised manuscript: 1) We emphasize the significance of exploring the relative binding affinities of citalopram to GLUT1, C5aR1, and SERT, as varying affinities could influence the drug’s overall efficacy. As highlighted in the current manuscript and our previous publication (PMID: 39388353), citalopram interacts with C5aR1 and GLUT1 through distinct binding sites and mechanisms, whereas its interaction with SERT is characterized by a more direct inhibition of serotonin binding (PMID: 27049939). To gain deeper insights into these interactions, employing techniques such as surface plasmon resonance or biolayer interferometry could provide valuable quantitative data on binding kinetics and affinities for each target. 2) We discuss how citalopram’s interactions with multiple targets may contribute to its therapeutic effects, particularly in the context of immune modulation and tumor progression. The potential for citalopram to exhibit diverse mechanisms of action through its interactions with these proteins warrants further investigation. A comprehensive understanding of these pathways could lead to the development of improved therapeutic strategies.

(c) GLUT1 knockdown in macrophages: In the revised manuscript, we revealed that TAMs predominantly express GLUT3 but not GLUT1 (Figures S8B and S8C). GLUT1 knockdown in THP-1 cells did not significantly impact their glycolytic metabolism (Figure S8D), whereas GLUT3 knockdown led to a marked reduction in glycolysis in THP-1 cells.

(d) Clinical data on SSRI use in HCC patients: Previously, we have reported that SSRIs use is associated with reduced disease progression in HCC patients (PMID: 39388353) (Cell Rep. 2024 Oct 22;43(10):114818.). As detailed below:

“We determined whether SSRIs for alleviating HCC are supported by real-world data. A total of 3061 patients with liver cancer were extracted from the Swedish Cancer Register. Among them, 695 patients had been administrated with post-diagnostic SSRIs. The Kaplan-Meier survival analysis suggested that patients who utilized SSRIs exhibited a significantly improved metastasis-free survival compared to those who did not use SSRIs, with a P value of log-rank test at 0.0002. Cox regression analysis showed that SSRI use was associated with a lower risk of metastasis (HR = 0.78; 95% CI, 0.62-0.99)”.

Reviewer #1 (Recommendations for the authors):

(1) Add experiments to address the questions listed in the weaknesses.

As suggested, related experiments are performed to strengthen the conclusions.

(2) It would be appreciated to show the expression profile of SERT or employ KO mouse models to eliminate the effect of SERT.

As suggested, analysis of a single-cell sequencing dataset of HCC (GSE125449) revealed that SERT is expressed not only in HCC cells but also in T cells, tumor-associated endothelial cells, and cancer-associated fibroblasts (Figure S2G). Consistently, SERT has been reported as an immune checkpoint restricting CD8 T cell antitumor immunity (PMID: 40403728). Furthermore, SERT KO mice (Cyagen Biosciences, S-KO-02549) was employed to investigate the effects of citalopram. However, the Slc6a4 gene knockout in mice resulted in a significant decrease in 5-HT levels in the brain and a lack of cortical columnar structures. Importantly, the mice exhibited an intolerance to citalopram treatment. Therefore, we did not pursue further investigation into the effects of citalopram in SERT KO mice.

(3) Due to the concern of specificity and animal health, it would be more direct if the authors could use, for example, C5ar1-fl/fl x Adgre1-Cre mouse models.

Thank you for your valuable suggestion. We fully agree with your comment regarding the value of introducing C5ar1-fl/fl and Adgre1-Cre mouse models, along with the necessary experimental setups, to substantiate this point. However, in our study, the C5ar1 KO mice exhibited normal overall appearance and viability, indicating that the model is generally healthy. Furthermore, we have validated the specific role of C5aR1 in macrophages through bone marrow reconstitution experiments, reinforcing the importance of C5aR1 in these cells. Therefore, we chose the current model to balance experimental effectiveness with considerations for animal health.

(4) For example, a GSEA or GO analysis of comparison of macrophages from C5ar1-/- or C5ar1+/- mice may point to the enriched pathway of phagocytosis in macrophages derived from C5ar1-/- rather than C5ar1+/- mice, and this information is helpful for the integrity of this work. Besides, it would be more reliable if a nucleus staining is included in Figures 3G and 3H.

As suggested, macrophages were isolated from tumor-bearing C5ar1^-/- and C5ar1^+/- mice and subsequently analyzed using RNA sequencing. The Gene Set Enrichment Analysis (GSEA) revealed a significant enrichment of the phagocytosis pathway in macrophages derived from C5ar1^-/- mice compared to those from C5ar1^+/- mice (see revised Figure S6A). While we acknowledge that the addition of a nucleus staining would enhance reliability, we would like to point out that this style of presentation is also commonly found in articles related to phagocytosis. Furthermore, this experiment involved a significant number of experimental mice, and in accordance with the 3Rs principle for animal experiments, we did not obtain additional sorted TAMs to perform the phagocytosis assay. Thank you for your understanding.

(5) In line 122, there is a typo, and it should be 'analysis'.

Thank you for pointing out the typo. It has been corrected to "analysis" in the revised manuscript.

(6) In line 217, there is no causal relationship between the contexts, and using 'as a result' may lead to misunderstanding.

As suggested, ‘as a result’ has been removed to avoid any misunderstanding.

(7) In line 322, please make sure if it should be HBS or PBS.

It is PBS, and revisions have been made.

(8) Figure S7, the calculation of cell proportions needs to use a consistent denominator.

As suggested, we calculated cell proportions using a consistent denominator (CD45⁺ cells).

(9) Figure 4C, label error.

Thanks for your careful review. It has been corrected to "MASH".

Reviewer #2 (Recommendations for the authors):

Dong et al. present compelling evidence for repurposing citalopram, a selective serotonin reuptake inhibitor (SSRI), as a potential therapeutic for hepatocellular carcinoma (HCC). While the concept of SSRI repurposing is not novel, this manuscript provides valuable insights into the drug's dual mechanisms: targeting tumor-associated macrophages (TAMs) via C5aR1 modulation and enhancing CD8+ T cell activity, alongside inhibiting cancer cell metabolism through GLUT1 suppression. The findings underscore the promise of drug repurposing strategies and identify C5aR1 as a noteworthy immunotherapeutic target. Addressing the following points will enhance the manuscript's impact and relevance to cancer immunotherapy.

Specific Comments:

(1) The authors identify C5aR1 on TAMs as a direct target of citalopram, independent of its classical SERT target, using drug-induced gene signature network analysis and co-immunofluorescence of CD163+ macrophages with C5aR1. The DARTS assay further supports the binding of C5aR1 to citalopram, complemented by in silico docking analysis adapted from their previous GLUT1 study. Since GLUT1 and SERT1 are transporter proteins while C5aR1 is a GPCR, these heterogeneous binding interactions suggest potential promiscuity in SSRI-target engagement.

(a) Figure 2A: The authors identify C5aR1 as a target using GSEA but do not specify the dataset used (e.g., cancer or immune cells) or the signature database consulted. Providing this context would enhance reproducibility.

For GSEA, we performed RNA sequencing (RNA-seq) on HCC-LM3 cells treated with citalopram or fluvoxamine and identified 114 differentially expressed genes (DEGs), which included 80 genes that were co-upregulated and 34 that were co-downregulated, as previously documented (PMID: 39388353). These DEGs were subsequently used to develop an SSRI-related gene signature. We then employed the RNA-seq data from liver hepatocellular carcinoma (LIHC) samples within The Cancer Genome Atlas (TCGA) cohort, which included 371 samples. HCC samples in the TCGA cohort were categorized into high and low expression groups based on the median expression levels of each candidate target gene, such as C5AR1. Finally, we conducted GSEA on the grouped samples (such as C5AR1-high versus C5AR1-low) using the SSRI-related gene signature. For reproducibility, detailed information has been added to the “Materials and Methods” section of the revised manuscript.

(b) Figure 2F: Given citalopram's reported role in inhibiting GLUT1, a comparative discussion on the relative contributions of GLUT1 inhibition versus C5aR1 modulation in tumor suppression is warranted. Performing a DARTS assay for GLUT1 in THP-1 cells, which express high GLUT1 levels and exhibit upregulation in M1 macrophages (https://doi.org/10.1038/s41467-022-33526-z), would clarify SSRI interactions with macrophage metabolism.

As suggested, we first investigated citalopram treatment in THP-1 cells. The result showed the glycolytic metabolism of THP-1 cells remained largely unaffected following citalopram treatment, as evidenced by glucose uptake, lactate release, and extracellular acidification rate (ECAR) (Figure S8A). Next, we mined a single cell sequencing datasets of HCC and revealed that TAMs predominantly express GLUT3 but not GLUT1 (Figure S8B). Consistently, Western blotting analysis showed a higher expression of GLUT3 and minimal levels of GLUT1 in THP-1 cells (Figure S8C). Consistently, it has been well documented that GLUT1 expression increased after M1 polarization stimuli an GLUT3 expression increased after M2 stimulation in macrophages (PMID: 37721853, PMID: 36216803). GLUT1 knockdown in THP-1 cells did not significantly impact their glycolytic metabolism (Figure S8D), whereas GLUT3 knockdown led to a marked reduction in glycolysis in THP-1 cells. Based on these findings, we conclude that the effects of citalopram on macrophages are primarily mediated through targeting C5aR1 rather than GLUT1.

(c) Figures 2H-I: A comparison of drug-protein interactions across GLUT1, C5aR1, and SERT1 would be valuable to identify potential shared or distinct binding features.

Citalopram exhibits distinct binding characteristics across its various targets, including GLUT1, C5aR1, and its classical target, SERT. In the case of C5aR1, our in silico docking analysis identified two key binding conformations at the orthosteric site. The interactions involved significant electrostatic contacts between citalopram’s amino group and negatively charged residues like E199 and D282. Notably, D282’s accessibility and orientation towards the binding cavity suggest it plays a crucial role in citalopram binding, highlighting the importance of specific amino acid interactions at this site. For GLUT1 (PMID: 39388353), citalopram’s interaction also demonstrated notable hydrophobic contacts, particularly through the fluorophenyl group with residues V328, P385, and L325. The cyanophtalane group penetrated the substrate-binding cavity, indicating that citalopram could occupy a similar binding site as glucose, which is distinct from the binding mechanism observed in C5aR1. The involvement of E380 in both poses for GLUT1 further emphasizes the role of electrostatic interactions in mediating citalopram’s binding to this transporter. In contrast, for SERT (PMID: 27049939), citalopram locks the transporter in an outward-open conformation by occupying the central binding site, which is located between transmembrane helices 1, 3, 6, 8 and 10. This binding directly obstructs serotonin from accessing its binding site, illustrating a more definitive blockade mechanism. Additionally, the allosteric site at SERT, positioned between extracellular loops 4 and 6 and transmembrane helices 1, 6, 10, and 11, enhances this blockade by sterically hindering ligand unbinding, thus providing a clear explanation for the allosteric modulation of serotonin transport. In summary, while citalopram interacts with C5aR1 and GLUT1 through distinct binding sites and mechanisms, its interaction with SERT is characterized by a more straightforward blockade of serotonin binding. The unique structural and functional attributes of each target highlight the versatility of citalopram and suggest that its pharmacological effects may vary significantly depending on the specific protein being targeted. In the revised manuscript, we have included detailed information in the revised manuscript.

(2) The manuscript presents evidence that citalopram reprograms TAMs to an anti-tumor phenotype, enhancing their phagocytic capacity.

(a) Bone Marrow Reconstitution Experiments (Figure 3): The use of donor (dC5aR1) and recipient (rC5aR1) mice is significant but requires clarification. Explicitly defining donor and recipient terminology and including a schematic of the experimental design would improve reader comprehension.

We appreciate your valuable feedback. As suggested, the terminology for donor (dC5aR1) and recipient (rC5aR1) mice was defined: “we injected GLUT1^KD Hepa1-6 cells into syngeneic recipient C5ar1^-/- (rC5ar1^-/- ) mice that had been reconstituted with donor C5ar1^+/- (dC5ar1^+/-) or C5ar1^-/- (dC5ar1^-/-) bone marrow (BM) cells to analyze the therapeutic effect of citalopram”. Additionally, we have included a schematic of the experimental design to enhance reader comprehension (see revised Figure 3E).

(b) GLUT1 Knockdown (KD) Tumor Cells: While GLUT1 KD tumor cells are utilized, the authors do not assess GLUT1 KD or knockout (KO) in macrophages. Testing the effect of citalopram on macrophages with GLUT1 KO/KD would help determine the relative importance of C5aR1 versus GLUT1 in mediating SSRI effects.

As responded above, GLUT1 knockdown in THP-1 cells did not significantly alter their glycolytic metabolism (Figure S8D). This observation can be explained by the predominant expression of GLUT3 in TAMs rather than GLUT1 (Figures S8B and S8C). Indeed, knockdown of GLUT3 led to a significant reduction in glycolysis in THP-1 cells (Figure S8C).

(c) C5aR1's Pro-Tumoral Role: The authors state that C5aR1 fosters an immunosuppressive microenvironment but omit a discussion of current literature on C5aR1's pro-tumoral role (e.g., https://doi.org/10.1038/s41467-024-48637-y, https://www.nature.com/articles/s41419-024-06500-4, https://doi.org/10.1016/j.ymthe.2023.12.010). Including this background in both the introduction and discussion would contextualize their findings.

Thanks for your valuable feedback. As suggested, we have revised the manuscript to include discussions on C5aR1’s pro-tumoral role, referencing the suggested studies in both the introduction and discussion sections for better context. As detailed below:

(1) Targeting C5aR1⁺ TAMs effectively reverses tumor progression and enhances anti-tumor response;

(2) Targeting C5aR1 reprograms TAMs from a protumor state to an antitumor state, promoting the secretion of CXCL9 and CXCL10 while facilitating the recruitment of cytotoxic CD8⁺ T cells;

(3) Moreover, citalopram induces TAM phenotypic polarization towards to a M1 proinflammatory state, which supports anti-tumor immune response within the TME.

(d) C5aR1 Expression in TAMs: Is C5aR1 expression constitutive in TAMs? Further details on C5aR1 expression dynamics in TAMs under different conditions could strengthen the discussion. Public datasets on TAMs in various states (e.g., https://www.nature.com/articles/s41586-023-06682-5, https://www.cell.com/cell/abstract/S0092-8674(19)31119-5, https://pubmed.ncbi.nlm.nih.gov/36657444/) may offer useful insights.

Thank you for your valuable suggestions. As suggested, we investigated the expression patterns of C5aR1 in TAMs using a HCC cohort (http://cancer-pku.cn:3838/HCC/). In the study conducted by Qiming Zhang et al. (PMID: 31675496), six distinct macrophage subclusters were identified, with M4-c1-THBS1 and M4-c2-C1QA showing significant enrichment in tumor tissues. M4-c1-THBS1 was enriched with signatures indicative of myeloid-derived suppressor cells (MDSCs), while M4-c2-C1QA exhibited characteristics that resembled those of TAMs as well as M1 and M2 macrophages. Our subsequent analysis revealed that C5aR1 is highly expressed in these two clusters, while expression levels in the other macrophage clusters were notably lower (see revised Figure S3).

(3) The manuscript shows that citalopram-induced reductions in systemic serotonin levels enhance CD8+ T cell activation and cytotoxicity, as evidenced by increased glycolytic metabolism and elevated IFN-γ, TNF-α, and GZMB expression.

(a) How CD8+ T cell activation is done in serotonin-deficient environments?

As reported (PMID: 34524861), one possible explanation is that serotonin may enhance PD-L1 expression on cancer cells, thereby impairing CD8⁺ T cell function. A deficiency of serotonin in the tumor microenvironment can delay tumor growth by promoting the accumulation and effector functions of CD8⁺ T cells while reducing PD-L1 expression. In addition to the SERT-mediated transport and 5-HT receptor signaling, CD8⁺ T cells can express TPH1 (PMID: 38215751, PMID: 40403728), enabling them to synthesize endogenous 5-HT, which activates their activity through serotonylation-dependent mechanisms (PMID: 38215751). In the revised manuscript, we have incorporated these interpretations.

(4) Suggestions for the model figure revision-C5aR1 in TAMs without Citalopram (Figure 5).

(a) Including a control scenario depicting receptor status and function in TAMs without citalopram treatment would provide a clearer baseline for understanding citalopram's effects.

Thank you for your valuable input regarding the model figure revision. We have included a revised mechanism model that depicts the receptor status and function of C5aR1 in TAMs without citalopram treatment, as you suggested.

(5) Suggestions for addressing clinical relevance.

The study predominantly uses preclinical mouse models, although some human HCC data is analyzed (Figures 2B and 3O). However, there is no discussion of clinical data on SSRI use in HCC patients.

Incorporating an analysis of patient survival outcomes based on SSRI treatment (e.g., https://pmc.ncbi.nlm.nih.gov/articles/PMC5444756/, https://pmc.ncbi.nlm.nih.gov/articles/PMC10483320/) would enhance the translational relevance of the findings.

Previously, we reported that the use of SSRIs is associated with reduced disease progression in HCC patients, based on real-world data from the Swedish Cancer Register (PMID: 39388353). As suggested, we have further discussed the clinical relevance of SSRIs in the revised manuscript. As detailed below:

“In a study involving 308,938 participants with HCC, findings indicated that the use of antidepressants following an HCC diagnosis was linked to a decreased risk of both overall mortality and cancer-specific mortality (PMID: 37672269). These associations were consistently observed across various subgroups, including different classes of antidepressants and patients with comorbidities such as hepatitis B or C infections, liver cirrhosis, and alcohol use disorders. Similarly, our analysis of real-world data from the Swedish Cancer Register demonstrated that SSRIs are correlated with slower disease progression in HCC patients (PMID: 39388353). Given these insights, antidepressants, especially SSRIs, show significant potential as anticancer therapies for individuals diagnosed with HCC”.

Author response:

Reviewer #1 (Public review):

Summary:

The authors examine the neural correlates of face recognition deficits in individuals with Developmental Prosopagnosia (DP; 'face blindness'). Contrary to theories that poor face recognition is driven by reduced spatial integration (via smaller receptive fields), here the authors find that the properties of receptive fields in face-selective brain regions are the same in typical individuals vs. those with DP. The main analysis technique is population Receptive Field (pRF) mapping, with a wide range of measures considered. The authors report that there are no differences in goodness-of-fit (R2), the properties of the pRFs (neither size, location, nor the gain and exponent of the Compressive Spatial Summation model), nor their coverage of the visual field. The relationship of these properties to the visual field (notably the increase in pRF size with eccentricity) is also similar between the groups. Eye movements do not differ between the groups.

Strengths:

Although this is a null result, the large number of null results gives confidence that there are unlikely to be differences between the two groups. Together, this makes a compelling case that DP is not driven by differences in the spatial selectivity of face-selective brain regions, an important finding that directly informs theories of face recognition. The paper is well written and enjoyable to read, the studies have clearly been carefully conducted with clear justification for design decisions, and the analyses are thorough.

Weaknesses:

One potential issue relates to the localisation of face-selective regions in the two groups. As in most studies of the neural basis of face recognition, localisers are used to find the face-selective Regions of Interest (ROIs) - OFA, mFus, and pFus, with comparison to the scene-selective PPA. To do so, faces are contrasted against other objects to find these regions (or scenes vs. others for the PPA). The one consistent difference that does emerge between groups in the paper is in the selectivity of these regions, which are less selective for faces in DP than in typical individuals (e.g., Figure 1B), as one might expect. 6/20 prosopagnosic individuals are also missing mFus, relative to only 2/20 typical individuals. This, to me, raises the question of whether the two groups are being compared fairly. If the localised regions were smaller and/or displaced in the DPs, this might select only a subset of the neural populations typically involved in face recognition. Perhaps the difference between groups lies outside this region. In other words, it could be that the differences in prosopagnosic face recognition lie in the neurons that are not able to be localised by this approach. The authors consider in the discussion whether their DPs may not have been 'true DPs', which is convincing (p. 12). The question here is whether the regions selected are truly the 'prosopagnosic brain areas' or whether there is a kind of survivor bias (i.e., the regions selected are normal, but perhaps the difference lies in the nature/extent of the regions. At present, the only consideration given to explain the differences in prosopagnosia is that there may be 'qualitative' differences between the two (which may be true), but I would give more thought to this.

We acknowledge that face-selective ROIs in DPs, relative to controls, may be smaller, less selective, or altogether missing when traditional methods of localization with fixed thresholds are used (Furl et al, 2011). For this reason - to circumvent potential survivor bias and ensure ROI voxel counts across participants are equated - we used a method of ROI definition whereby each subject’s individual statistical map from the localizer was intersected with a generously-sized group mask for each ROI and the top 20% most category-selective voxels were retained for the pRF analysis (Norman-Haignere et al., 2013; Jiahui et al., 2018). This means that the raw number of voxels per ROI was equal across all participants with respect to the common group space, thereby ensuring a fair comparison even in cases where one group shows diminished category-selectivity. The details of the ROI definition are provided in the Methods at the end of the manuscript. To ensure readers understand our approach, we will also make more explicit mention of this in the main body of the manuscript. 

With regard to the question of whether face-selective ROIs may be displaced in DPs compared to controls, previous work from the senior author’s lab (Jiahui et al., 2018) shows that, despite exhibiting weaker activations, the peak coordinates of significant clusters in DPs occupy very similar locations to those of controls. And, even if there were indeed slight displacements of face-selective ROIs for some subjects, the group-defined masks used in the present analysis were large enough to capture the majority of the top voxels. In the supplemental materials section, we will include a diagram of the group masks used in our study.

The reviewer here also points out that more DPs than controls were missing the mFUS region (6/20 DPs vs 2/20 controls; Figure 1C). However, ‘missing’ in this context was not based on face-selectivity but rather a lack of retinotopic tuning. PRFs were fit to all voxels within each ROI - with all subjects starting out with equal voxel counts - and thereafter, voxels for which the variance explained by the pRF model was below 20% were excluded from subsequent analysis. We decided that any ROI with fewer than 10 voxels remaining after thresholding on the pRF fit should be deemed ‘missing’ since we considered the amount of data insufficient to reliably characterize the region’s retinotopic profile. While it may be somewhat interesting that four more DPs than controls were ‘missing’ left mFUS, using this particular set of decision criteria, it is important to keep in mind that left mFUS was just one of six face-selective regions under study. The other five regions, many of which evinced strong fits by the pRF model, were represented comparably in DPs and controls and showed high similarity in the pRF parameters. Furthermore, across most participants, mFUS exhibited a low proportion of retinotopically modulated voxels (defined as voxels with pRF R squared greater than 20%, see Figure 1D). A follow-up analysis showed that the count of voxels surviving pRF R squared thresholding in left mFUS was not significantly correlated with mean pRF size (r(30)=0.23, t=1.28,  p=0.21) indicating that the greater exclusion of DPs in this region is unlikely to have biased the group’s average pRF size.

The discussion considers the differences between the current study and an unpublished preprint (Witthoft et al, 2016), where DPs were found to have smaller pRFs than typical individuals. The discussion presents the argument that the current results are likely more robust, given the use of images within the pRF mapping stimuli here (faces, objects, etc) as opposed to checkerboards in the prior work, and the use of the CSS model here as opposed to a linear Gaussian model previously. This is convincing, but fails to address why there is a lack of difference in the control vs. DP group here. If anything, I would have imagined that the use of faces in mapping stimuli would have promoted differences between the groups (given the apparent difference in selectivity in DPs vs. controls seen here), which adds to the reliability of the present result. Greater consideration of why this should have led to a lack of difference would be ideal. The latter point about pRF models (Gaussian vs. CSS) does seem pertinent, for instance - could the 'qualitative' difference lead to changes in the shape of these pRFs in prosopagnosia that are better characterised by the CSS model, perhaps? Perhaps more straightforwardly, and related to the above, could differences in the localisation of face-selective regions have driven the difference in prior work compared to here?

We agree that the use of high-level mapping stimuli (including faces) adds to the reliability of the present results for DPs and could have further emphasized differences between the groups if true differences did, in fact, exist. We speculate on the extent to which the type of mapping stimuli and various other methodological factors (e.g. stimulus size, aperture design, pRF model) could have explained the divergent findings in our study versus that of Witthoft et al. (2016) in the section of the Discussion titled, “What factors may have contributed to the different results for the present study and Witthoft et al. (2016)”. In brief, our use of more colorful, naturalistic stimuli targeting higher-level visual areas elicited better model fits than the black and white checkerboard pattern used by Witthoft et al. (2016). The CSS model we used is better suited for higher-level regions and makes fewer assumptions than the linear pRF model. The field of view of our stimulus was smaller but still relevant for real-world perception of faces. Finally, our aperture design and longer run length likely also improved reliability. Overall, these methodological improvements, along with our larger sample size, provide stronger evidence for our findings. These are our best attempts to make sense of the divergent findings, but it is not possible to come to a definitive explanation. Examples abound of exaggerated or spurious effects from small-scale studies that ultimately fail to replicate in the related field of dyslexia research (Jednorog et al., 2015; Ramus et al., 2018) and neuroimaging research more generally (Turner et al., 2018; Poldrack et al., 2017). Sometimes there are clear explanations for a lack of replicability (e.g. software bugs, overly flexible preprocessing methods, etc.), but many times the real reason cannot be determined.

Regarding the type of pRF model deployed, our use of a non-linear exponent (versus a linear model as in the Witthoft et al. (2016) preprint) is unlikely to explain the similarity we observed between the groups in terms of pRF size. Specifically, the groups did not show substantial differences in the exponent by ROI, as seen in Figure 1E, so the use of a linear model should, in theory, produce similar outcomes for the two groups. We will mention this point in the main text.

Finally, the lack of variations in the spatial properties of these brain regions is interesting in light of the theories that spatial integration is a key aspect of effective face recognition. In this context, it is interesting to note the marked drop in R2 values in face-selective regions like mFus relative to earlier cortex. The authors note in some sense that this is related to the larger receptive field size, but is there a broader point here that perhaps the receptive field model (even with Compressive Spatial Summation) is simply a poor fit for the function of these areas? Could it be that these areas are simply not spatial at all? A broader link between the null results presented here and their implications for theories of face recognition would be ideal.

The weaker pRF fits found in mFUS, to us, raise the question of whether there is a more effective pRF stimulus for these more anterior regions. For example, it might be possible to obtain higher and more reliable responses there using single isolated faces (Cf. Kay, Weiner, Grill-Spector, 2015). More broadly, though, we agree that it is important to acknowledge that the receptive field model might ultimately be a coarse and incomplete characterization of neural function in these areas. As the other reviewer suggests, one possibility is that other brain processes (e.g. functional or structural connectivity between ROIs) may give rise to holistic face processing in ways that are not captured by pRF properties.

Reviewer #2 (Public review):

Summary:

This is a well-conducted and clearly written manuscript addressing the link between population receptive fields (pRFs) and visual behavior. The authors test whether developmental prosopagnosia (DP) involves atypical pRFs in face-selective regions, a hypothesis suggested by prior work with a small DP sample. Using a larger cohort of DPs and controls, robust pRF mapping with appropriate stimuli and CSS modeling, and careful in-scanner eye tracking, the authors report no group differences in pRF properties across the visual processing hierarchy. These results suggest that reduced spatial integration is unlikely to account for holistic face processing deficits in DP.

Strengths:

The dataset quality, sample size, and methodological rigor are notable strengths.

Weaknesses:

The primary concern is the interpretation of the results.

(1) Relationship between pRFs and spatial integration

While atypical pRF properties could contribute to deficits in spatial integration, impairments in holistic processing in DPs are not necessarily caused by pRF abnormalities. The discussion could be strengthened by considering alternative explanations for reduced spatial integration, such as altered structural or functional connectivity in the face network, which has been reported to underlie DP's difficulties in integrating facial features.

We agree the Discussion section could benefit from mentioning that alterations to other neural mechanisms, besides pRF organization, could produce deficits in holistic processing. This could take the form of altered functional connectivity (Rosenthal et al., 2017; Lohse et al., 2016; Avidan et al., 2014) or altered structural connectivity (Gomez et al., 2015; Song et al., 2015)

(2) Beyond the null hypothesis testing framework

The title claims "normal spatial integration," yet this conclusion is based on a failure to reject the null hypothesis, which does not justify accepting the alternative hypothesis. To substantiate a claim of "normal," the authors would need to provide analyses quantifying evidence for the absence of effects, e.g., using a Bayesian framework.

We acknowledge that, using frequentist statistical methods, failing to reject the null hypothesis is not sufficient to claim equivalence. For the revision, we will look into additional analyses that could quantify evidence for the null hypothesis. And we will adjust the wording of the title in this regard.

(3) Face-specific or broader visual processing

Prior work from the senior author's lab (Jiahui et al., 2018) reported pronounced reductions in scene selectivity and marginal reductions in body selectivity in DPs, suggesting that visual processing deficits in DPs may extend beyond faces. While the manuscript includes PPA as a high-level control region for scene perception, scene selectivity was not directly reported. The authors could also consider individual differences and potential data-quality confounds (tSNR difference between and within groups, several obvious outliers in the figures, etc). For instance, examining whether reduced tSNR in DPs contributed to lower face selectivity in the DP group in this dataset.

Thank you for this suggestion - we will compare tSNR between the groups as a measure of data quality and we will include these comparisons. A preliminary look indicates that both groups possessed similar distributions of tSNR across many of the face-selective regions investigated here.

(4) Linking pRF properties to behavior

The manuscript aims to examine the relationship between pRF properties and behavior, but currently reports only one aspect of pRF (size) in relation to a single behavioral measure (CFMT), without full statistical reporting:

"We found no significant association between participants' CFMT scores and mean pRF size in OFA, pFUS, or mFUS."

For comprehensive reporting, the authors could examine additional pRF properties (e.g., center, eccentricity, scaling between eccentricity and pRF size, shape of visual field coverage, etc), additional ROIs (early, intermediate, and category-selective areas), and relate them to multiple behavioral measures (e.g., HEVA, PI20, FFT). This would provide a full picture of how pRF characteristics relate to behavioral performance in DP.

We will report the full statistical values (r, p) for the (albeit non-significant) relationship between CFMT score and pRF size - thank you for bringing that to our attention. Additionally, we will add other analyses assessing the relationship between a wider array of pRF measures and the other behavioral tests administered to provide a more comprehensive picture of the relation between pRFs and behavior.

References:

Avidan, G., Tanzer, M., Hadj-Bouziane, F., Liu, N., Ungerleider, L. G., & Behrmann, M. (2014). Selective Dissociation Between Core and Extended Regions of the Face Processing Network in Congenital Prosopagnosia. Cerebral Cortex, 24(6), 1565–1578. https://doi.org/10.1093/cercor/bht007

Furl, N., Garrido, L., Dolan, R. J., Driver, J., & Duchaine, B. (2011). Fusiform gyrus face selectivity relates to individual differences in facial recognition ability. Journal of Cognitive Neuroscience, 23(7), 1723–1740. https://doi.org/10.1162/jocn.2010.21545

Gomez, J., Pestilli, F., Witthoft, N., Golarai, G., Liberman, A., Poltoratski, S., Yoon, J., & Grill-Spector, K. (2015). Functionally Defined White Matter Reveals Segregated Pathways in Human Ventral Temporal Cortex Associated with Category-Specific Processing. Neuron, 85(1), 216–227. https://doi.org/10.1016/j.neuron.2014.12.027

Jednoróg, K., Marchewka, A., Altarelli, I., Monzalvo Lopez, A. K., van Ermingen-Marbach, M., Grande, M., Grabowska, A., Heim, S., & Ramus, F. (2015). How reliable are gray matter disruptions in specific reading disability across multiple countries and languages? Insights from a large-scale voxel-based morphometry study. Human Brain Mapping, 36(5), 1741–1754. https://doi.org/10.1002/hbm.22734

Jiahui, G., Yang, H., & Duchaine, B. (2018). Developmental prosopagnosics have widespread selectivity reductions across category-selective visual cortex. Proceedings of the National Academy of Sciences of the United States of America, 115(28), E6418–E6427. https://doi.org/10.1073/pnas.1802246115

Kay, K. N., Weiner, K. S., Kay, K. N., & Weiner, K. S. (2015). Attention Reduces Spatial Uncertainty in Human Ventral Temporal Cortex Attention Reduces Spatial Uncertainty in Human Ventral Temporal Cortex. Current Biology, 25(5), 595–600. https://doi.org/10.1016/j.cub.2014.12.050

Lohse, M., Garrido, L., Driver, J., Dolan, R. J., Duchaine, B. C., & Furl, N. (2016). Effective connectivity from early visual cortex to posterior occipitotemporal face areas supports face selectivity and predicts developmental prosopagnosia. Journal of Neuroscience, 36(13), 3821–3828. https://doi.org/10.1523/JNEUROSCI.3621-15.2016

Norman-Haignere, S., Kanwisher, N., & McDermott, J. H. (2013). Cortical pitch regions in humans respond primarily to resolved harmonics and are located in specific tonotopic regions of anterior auditory cortex. Journal of Neuroscience, 33(50), 19451–19469. https://doi.org/10.1523/JNEUROSCI.2880-13.2013

Poldrack, R. A., Baker, C. I., Durnez, J., Gorgolewski, K. J., Matthews, P. M., Munafò, M. R., Nichols, T. E., Poline, J. B., Vul, E., & Yarkoni, T. (2017). Scanning the horizon: Towards transparent and reproducible neuroimaging research. Nature Reviews Neuroscience, 18(2), 115–126. https://doi.org/10.1038/nrn.2016.167

Ramus, F., Altarelli, I., Jednoróg, K., Zhao, J., & Scotto di Covella, L. (2018). Neuroanatomy of developmental dyslexia: Pitfalls and promise. Neuroscience and Biobehavioral Reviews, 84(July 2017), 434–452. https://doi.org/10.1016/j.neubiorev.2017.08.001

Rosenthal, G., Tanzer, M., Simony, E., Hasson, U., Behrmann, M., & Avidan, G. (2017). Altered topology of neural circuits in congenital prosopagnosia. ELife, 6, 1–20. https://doi.org/10.7554/eLife.25069

Song, S., Garrido, L., Nagy, Z., Mohammadi, S., Steel, A., Driver, J., Dolan, R. J., Duchaine, B., & Furl, N. (2015). Local but not long-range microstructural differences of the ventral temporal cortex in developmental prosopagnosia. Neuropsychologia, 78, 195–206. https://doi.org/10.1016/j.neuropsychologia.2015.10.010

Turner, B. O., Paul, E. J., Miller, M. B., & Barbey, A. K. (2018). Small sample sizes reduce the replicability of task-based fMRI studies. Communications Biology, 1(1). https://doi.org/10.1038/s42003-018-0073-z

Witthoft, N., Poltoratski, S., Nguyen, M., Golarai, G., Liberman, A., LaRocque, K., Smith, M., & Grill-Spector, K. (2016). Reduced spatial integration in the ventral visual cortex underlies face recognition deficits in developmental prosopagnosia. BioRxiv, 1–26.

Author response:

We would like to thank the reviewers for their valuable feedback on this research.

Based on the limitations identified across the reviews, we will make four major revisions to this work. We will: (1) run a multi-step experiment to better test the successor representation framework and the predictions made by our model simulations; (2) include a task to explicitly gauge participants’ judgements about the relatedness of the robot features; (3) test additional computational models that may better capture participants’ behavior; and (4) clarify and expand the definition of the inductive bias studied in this work.

(1) The reviews raised the concern that while we frame our results as being about predictive learning within the successor representation framework, we investigated participants’ behavior on a one-step task that is not well suited to characterizing this form of predictive representation. Moreover, our simulations make predictions about how learning may differ in relatively more naturalistic environments, yet we do not test human participants in these more complex learning contexts. Finally, we found several null results for effects that were predicted by our simulations. This may be because the benefits of the bias are predicted to be more limited in simpler learning environments, and our experiment may not have been sufficiently powered to detect these smaller effects. To address these limitations, we will run a new experiment with a multi-step causal structure, allowing us to better test the SR framework while more comprehensively investigating the predictions of the simulations and improving our power to detect effects that were null in the one-step experiment.

(2) We argued that the causal-bias parameter may capture idiosyncratic differences in participants’ semantic memory that had an ensuing effect on their learning. However, the reviews identified that we did not explicitly measure participants’ judgements about the relatedness of the robot features to verify that existing conceptual knowledge drove these individual differences. In the new experiment, we will therefore include a task to quantify participants’ individual judgements about the relatedness of the robot features.

(3) The reviews questioned the suitability of the feature-based model for explaining behavior in the task given that only a subset of participants were best fit by the model, and not all of the model’s behavioral predictions were observed in the human subjects experiment. The reviews suggested alternative models could more validly capture behavior. In the revision, we will therefore consider alternative models (e.g., model-based planning, successor features with decay on weak associations).

(4) The reviews requested some clarity around our conceptualization of the inductive bias studied in this work, and questioned whether the task sufficiently captured the richness of semantic knowledge that may be required for a “semantic bias.” We acknowledge that the term semantic bias may not be an accurate descriptor of the inductive bias we measured. Instead, a more general “conceptual bias” term may better capture how any hierarchical conceptual knowledge – semantic or otherwise – may drive the studied bias. We will clarify our terminology in the revision.

In addition to these major revisions, we will address more minor critiques and suggestions raised by individual reviewers.

Author response:

We thank you and the reviewers for the careful assessment and for the thoughtful public reviews of our manuscript. We are encouraged that the novelty of the observations and the systematic nature of our approach are recognised, and we fully appreciate the concerns raised regarding potential artefacts and the incompletely defined mechanism.

(1) Context for funding (Reviewer #2)

In response to Reviewer #2’s note that this study is personally funded by one of the authors, we would like to provide some context. When wefirst observed that high-NaCl treatment caused a reversible loss ofactivation-loop phospho-signal for PKN1, we recognised its potential importance and submitted grant applications specifically to investigate this phenomenon. Unfortunately, these applications were not funded. As a result, as Reviewer #2 correctly points out, we have continued this work only modestly, using a personal donation from one of the authors to the university.

Our initial view that this phenomenon merited detailed study was based mainly on three points:

(i) Phosphorylation of the activation-loop threonine is critical for the catalytic activity of these kinases.

(ii) In previous work on PKN, no stress signal had been identified that could induce such a prominent and rapid change in activation-loop threonine phosphorylation.

(iii) Although the phenomenon was originally detected under high Na⁺ conditions, if it simply reflected the balance between phosphorylation and dephosphorylation, then it seemed plausible that more physiological changes in ion concentrations might drive signals in cells.

To explore point (iii), we initially attempted to define the ion concentrations that trigger dephosphorylation under conditions where re-phosphorylation was blocked. However, even with potent kinase inhibitors, we were unable to prevent recovery of the phospho-signal.This unexpected result prompted us to investigate the underlying mechanism of this unusual behaviour in more depth.

(2) Hidden artefacts and mass-spectrometric approaches  We fully share the reviewers’ concern expressed as “We remain concerned about hidden artifacts.” Throughout this work, we have repeatedly asked ourselves whether the phenomenon could arise from something as trivial as an artefact inherent to immunoblotting or from an unrecognised flaw in our experimental design, or whether it might ultimately be explainable in terms of conventional rules of protein phosphorylation' and 'dephosphorylation'.

To capture the phenomenon from an additional, independent angle, we agree with the reviewers’ suggestion to attempt mass spectrometry–based analysis. However, there are several substantial technical hurdles:

(i) At present, the phenomenon strictly requires the presence of animal cell extracts; we have not been able to reproduce it in their absence.

(ii) When we attempt to repurify the activation-loop fragments after ion treatment, the phosphate group is re-acquired during the wash steps, even when we use the same high-salt buffer employed for ion treatment.

(iii) In global phosphoproteomic analyses, reliably detecting a specific change in phosphorylation at a defined site is technically demanding and costly.

We therefore hope to identify conditions under which we can both (a)preserve the phosphorylation state established by the ion treatmentduring sample handling, and (b) achieve sufficient purification for informative mass spectrometric analysis. Reviewer #3 raised an important question regarding the origin of the two bands observed in Figure 6C. At present, we do not have data that would allow us to address this point in a well-founded manner. We hope that successful mass spectrometric analysis will also enable us to comment more concretely on this issue.

(3) Role of PP2A and reconstitution experimentsAs emphasised by Reviewers #1 and #3, although PP2A appears to beessential for the phenomenon, we have not yet been able to formulate a mechanistically plausible model that incorporates PP2A in a satisfactory way, and we share the reviewers’ concern on this point. We performed preliminary in vitro reconstitution experiments using recombinant PP2A purified from Sf9 cells (comprising the catalytic C subunit, the scaffold A subunit, and GST-fused PR130 as a B subunit) together with purified PKN1 activation loop fragments, to test whether the phenomenon can be reconstituted under low- and high-KCl conditions. Under the conditions tested so far, we have not yet succeeded in reconstituting the salt-dependent loss and recovery of activation loop phosphorylation. In vivo, PP2A holoenzymes exhibit substantial diversity in their subunit composition, particularly in the B subunit, and it is therefore unclear whether the particular complex we used is the one responsible for the behaviour observed in lysates. We plan to test additional PP2A complexes and, in parallel, to examine the effect of adding bacterial cell extracts—which by themselves do not induce changes in activation-loop phosphorylation in our system—in order to determine whether additional eukaryotic factors are required for reconstitution.

Through these experiments, we hope to move closer to constructing amechanistic scheme that explicitly includes PP2A and clarifies its role in this unusual process of phosphate loss and reacquisition.

We are grateful for the constructive feedback and believe these planned revisions will strengthen the clarity, balance, and rigour of our study.

Author response:

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

I thank the authors for their clarifications. The manuscript is much improved now, in my opinion. The new power spectral density plots and revised Figure 1 are much appreciated. However, there is one remaining point that I am unclear about. In the rebuttal, the authors state the following: "To directly address the question of whether the auditory signal was distracting, we conducted a follow-up MEG experiment. In this study, we observed a significant reduction in visual accuracy during the second block when the distractor was present (see Fig. 7B and Suppl. Fig. 1B), providing clear evidence of a distractor cost under conditions where performance was not saturated." 

I am very confused by this statement, because both Fig. 7B and Suppl. Fig. 1B show that the visual- (i.e., visual target presented alone) has a lower accuracy and longer reaction time than visual+ (i.e., visual target presented with distractor). In fact, Suppl. Fig. 1B legend states the following: "accuracy: auditory- - auditory+: M = 7.2 %; SD = 7.5; p = .001; t(25) = 4.9; visual- - visual+: M = -7.6%; SD = 10.80; p < .01; t(25) = -3.59; Reaction time: auditory- - auditory +: M = -20.64 ms; SD = 57.6; n.s.: p = .08; t(25) = -1.83; visual- - visual+: M = 60.1 ms ; SD = 58.52; p < .001; t(25) = 5.23)." 

These statements appear to directly contradict each other. I appreciate that the difficulty of auditory and visual trials in block 2 of MEG experiments are matched, but this does not address the question of whether the distractor was actually distracting (and thus needed to be inhibited by occipital alpha). Please clarify.

We apologize for mixing up the visual and auditory distractor cost in our rebuttal. The reviewer is right in that our two statements contradict each other.

To clarify: In the EEG experiment, we see significant distractor cost for auditory distractors in the accuracy (which can be seen in SUPPL Fig. 1A). We also see a faster reaction time with auditory distractors, which may speak to intersensory facilitation. As we used the same distractors for both experiments, it can be assumed that they were distracting in both experiments.

In our follow-up MEG-experiment, as the reviewer stated, performance in block 2 was higher than in block 1, even though there were distractors present. In this experiment, distractor cost and learning effects are difficult to disentangle. It is possible that participants improved over time for the visual discrimination task in Block 1, as performance at the beginning was quite low. To illustrate this, we divided the trials of each condition into bins of 10 and plotted the mean accuracy in these bins over time (see Author response image 1). Here it can be seen that in Block 2, there is a more or less stable performance over time with a variation < 10 %. In Block 1, both for visual as well as auditory trials, an improvement over time can be seen. This is especially strong for visual trials, which span a difference of > 20%. Note that the mean performance for the 80-90 trial bin was higher than any mean performance observed in Block 2. 

Additionally, the same paradigm has been applied in previous investigations, which also found distractor costs for the here-used auditory stimuli in blocked and non-blocked designs. See:

Mazaheri, A., van Schouwenburg, M. R., Dimitrijevic, A., Denys, D., Cools, R., & Jensen, O. (2014). Region-specific modulations in oscillatory alpha activity serve to facilitate processing in the visual and auditory modalities. NeuroImage, 87, 356–362. https://doi.org/10.1016/j.neuroimage.2013.10.052

Van Diepen, R & Mazaheri, A 2017, 'Cross-sensory modulation of alpha oscillatory activity: suppression, idling and default resource allocation', European Journal of Neuroscience, vol. 45, no. 11, pp. 1431-1438. https://doi.org/10.1111/ejn.13570

Author response image 1.

Accuracy development over time in the MEG experiment. During block 1, a performance increase over time can be observed for visual as well as for auditory stimuli. During Block 2, performance is stable over time. Data are presented as mean ± SEM. N = 27 (one participant was excluded from this analysis, as their trial count in at least one condition was below 90 trials).

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

In this study, Brickwedde et al. leveraged a cross-modal task where visual cues indicated whether upcoming targets required visual or auditory discrimination. Visual and auditory targets were paired with auditory and visual distractors, respectively. The authors found that during the cue-to-target interval, posterior alpha activity increased along with auditory and visual frequency-tagged activity when subjects were anticipating auditory targets. The authors conclude that their results disprove the alpha inhibition hypothesis, and instead implies that alpha "regulates downstream information transfer." However, as I detail below, I do not think the presented data irrefutably disproves the alpha inhibition hypothesis. Moreover, the evidence for the alternative hypothesis of alpha as an orchestrator for downstream signal transmission is weak. Their data serves to refute only the most extreme and physiologically implausible version of the alpha inhibition hypothesis, which assumes that alpha completely disengages the entire brain area, inhibiting all neuronal activity.

We thank the reviewer for taking the time to provide additional feedback and suggestions and we improved our manuscript accordingly.

(1) Authors assign specific meanings to specific frequencies (8-12 Hz alpha, 4 Hz intermodulation frequency, 36 Hz visual tagging activity, 40 Hz auditory tagging activity), but the results show that spectral power increases in all of these frequencies towards the end of the cue-to-target interval. This result is consistent with a broadband increase, which could simply be due to additional attention required when anticipating auditory target (since behavioral performance was lower with auditory targets, we can say auditory discrimination was more difficult). To rule this out, authors will need to show a power spectral density curve with specific increases around each frequency band of interest. In addition, it would be more convincing if there was a bump in the alpha band, and distinct bumps for 4 vs 36 vs 40 Hz band.

This is an interesting point with several aspects, which we will address separately

Broadband Increase vs. Frequency-Specific Effects:

The suggestion that the observed spectral power increases may reflect a broadband effect rather than frequency-specific tagging is important. However, Supplementary Figure 11 shows no difference between expecting an auditory or visual target at 44 Hz. This demonstrates that (1) there is no uniform increase across all frequencies, and (2) the separation between our stimulation frequencies was sufficient to allow differentiation using our method.

Task Difficulty and Performance Differences:

The reviewer suggests that the observed effects may be due to differences in task difficulty, citing lower performance when anticipating auditory targets in the EEG study. This issue was explicitly addressed in our follow-up MEG study, where stimulus difficulty was calibrated. In the second block—used for analysis—accuracy between auditory and visual targets was matched (see Fig. 7B). The replication of our findings under these controlled conditions directly rules out task difficulty as the sole explanation. This point is clearly presented in the manuscript.

Power Spectrum Analysis:

The reviewer’s suggestion that our analysis lacks evidence of frequency-specific effects is addressed directly in the manuscript. While we initially used the Hilbert method to track the time course of power fluctuations, we also included spectral analyses to confirm distinct peaks at the stimulation frequencies. Specifically, when averaging over the alpha cluster, we observed a significant difference at 10 Hz between auditory and visual target expectation, with no significant differences at 36 or 40 Hz in that cluster. Conversely, in the sensor cluster showing significant 36 Hz activity, alpha power did not differ, but both 36 Hz and 40 Hz tagging frequencies showed significant effects These findings clearly demonstrate frequency-specific modulation and are already presented in the manuscript.

(2) For visual target discrimination, behavioral performance with and without the distractor is not statistically different. Moreover, the reaction time is faster with distractor. Is there any evidence that the added auditory signal was actually distracting?

We appreciate the reviewer’s observation regarding the lack of a statistically significant difference in behavioral performance for visual target discrimination with and without the auditory distractor. While this was indeed the case in our EEG experiment, we believe the absence of an accuracy effect may be attributable to a ceiling effect, as overall visual performance approached 100%. This high baseline likely masked any subtle influence of the distractor.

To directly address the question of whether the auditory signal was distracting, we conducted a follow-up MEG experiment. In this study, we observed a significant reduction in visual accuracy during the second block when the distractor was present (see Fig. 7B and Suppl. Fig. 1B), providing clear evidence of a distractor cost under conditions where performance was not saturated.

Regarding the faster reaction times observed in the presence of the auditory distractor, this phenomenon is consistent with prior findings on intersensory facilitation. Auditory stimuli, which are processed more rapidly than visual stimuli, can enhance response speed to visual targets—even when the auditory input is non-informative or nominally distracting (Nickerson, 1973; Diederich & Colonius, 2008; Salagovic & Leonard, 2021). Thus, while the auditory signal may facilitate motor responses, it can simultaneously impair perceptual accuracy, depending on task demands and baseline performance levels.

Taken together, our data suggest that the auditory signal does exert a distracting influence, particularly under conditions where visual performance is not at ceiling. The dual effect—facilitated reaction time but reduced accuracy—highlights the complexity of multisensory interactions and underscores the importance of considering both behavioral and neurophysiological measures.

(3) It is possible that alpha does suppress task-irrelevant stimuli, but only when it is distracting. In other words, perhaps alpha only suppresses distractors that are presented simultaneously with the target. Since the authors did not test this, they cannot irrefutably reject the alpha inhibition hypothesis.

The reviewer’s claim that we did not test whether alpha suppresses distractors presented simultaneously with the target is incorrect. As stated in the manuscript and supported by our data (see point 2), auditory distractors were indeed presented concurrently with visual targets, and they were demonstrably distracting. Therefore, the scenario the reviewer suggests was not only tested—it forms a core part of our design.

Furthermore, it was never our intention to irrefutably reject the alpha inhibition hypothesis. Rather, our aim was to revise and expand it. If our phrasing implied otherwise, we have now clarified this in the manuscript. Specifically, we propose that alpha oscillations:

(a) Exhibit cyclic inhibitory and excitatory dynamics;

(b) Regulate processing by modulating transfer pathways, which can result in either inhibition or facilitation depending on the network context.

In our study, we did not observe suppression of distractor transfer, likely due to the engagement of a supramodal system that enhances both auditory and visual excitability. This interpretation is supported by prior findings (e.g., Jacoby et al., 2012), which show increased visual SSEPs under auditory task load, and by Zhigalov et al. (2020), who found no trial-by-trial correlation between alpha power and visual tagging in early visual areas, despite a general association with attention.

Recent evidence (Clausner et al., 2024; Yang et al., 2024) further supports the notion that alpha oscillations serve multiple functional roles depending on the network involved. These roles include intra- and inter-cortical signal transmission, distractor inhibition, and enhancement of downstream processing (Scheeringa et al., 2012; Bastos et al., 2015; Zumer et al., 2014). We believe the most plausible account is that alpha oscillations support both functions, depending on context.

To reflect this more clearly, we have updated Figure 1 to present a broader signal-transfer framework for alpha oscillations, beyond the specific scenario tested in this study.

We have now revised Figure 1 and several sentences in the introduction and discussion, to clarify this argument.

L35-37: Previous research gave rise to the prominent alpha inhibition hypothesis, which suggests that oscillatory activity in the alpha range (~10 Hz) plays a mechanistic role in selective attention through functional inhibition of irrelevant cortical areas (see Fig. 1; Foxe et al., 1998; Jensen & Mazaheri, 2010; Klimesch et al., 2007).

L60-65: In contrast, we propose that functional and inhibitory effects of alpha modulation, such as distractor inhibition, are exhibited through blocking or facilitating signal transmission to higher order areas (Peylo et al., 2021; Yang et al., 2023; Zhigalov & Jensen, 2020; Zumer et al., 2014), gating feedforward or feedback communication between sensory areas (see Fig. 1; Bauer et al., 2020; Haegens et al., 2015; Uemura et al., 2021).

L482-485: This suggests that responsiveness of the visual stream was not inhibited when attention was directed to auditory processing and was not inhibited by occipital alpha activity, which directly contradicts the proposed mechanism behind the alpha inhibition hypothesis.

L517-519: Top-down cued changes in alpha power have now been widely viewed to play a functional role in directing attention: the processing of irrelevant information is attenuated by increasing alpha power in areas involved with processing this information (Foxe, Simpson, & Ahlfors, 1998; Hanslmayr et al., 2007; Jensen & Mazaheri, 2010).

L566-569: As such, it is conceivable that alpha oscillations can in some cases inhibit local transmission, while in other cases, depending on network location, connectivity and demand, alpha oscillation can facilitate signal transmission. This mechanism allows to increase transmission of relevant information and to block transmission of distractors.

(4) In the abstract and Figure 1, the authors claim an alternative function for alpha oscillations; that alpha "orchestrates signal transmission to later stages of the processing stream." In support, the authors cite their result showing that increased alpha activity originating from early visual cortex is related to enhanced visual processing in higher visual areas and association areas. This does not constitute a strong support for the alternative hypothesis. The correlation between posterior alpha power and frequency-tagged activity was not specific in any way; Fig. 10 shows that the correlation appeared on both 1) anticipating-auditory and anticipating-visual trials, 2) the visual tagged frequency and the auditory tagged activity, and 3) was not specific to the visual processing stream. Thus, the data is more parsimonious with a correlation than a causal relationship between posterior alpha and visual processing.

Again, the reviewer raises important points, which we want to address

The correlation between posterior alpha power and frequency-tagged activity was not specific, as it is present both when auditory and visual targets are expected:

If there is a connection between posterior alpha activity and higher-order visual information transfer, then it can be expected that this relationship remains across conditions and that a higher alpha activity is accompanied by higher frequency-tagged activity, both over trials and over conditions. However, it is possible that when alpha activity is lower, such as when expecting a visual target, the signal-to-noise ratio is affected, which may lead to higher difficulty to find a correlation effect in the data when using non-invasive measurements.

The connection between alpha activity and frequency-tagged activity appears both for auditory as well as visual stimuli and The correlation is not specific to the visual processing stream:

While we do see differences between conditions (e.g. in the EEG-analysis, mostly 36 Hz correlated with alpha activity and only in one condition 40 Hz showed a correlation as well), it is true that in our MEG analysis, we found correlations both between alpha activity and 36 Hz as well as alpha activity and 40 Hz.  

We acknowledge that when analysing frequency-tagged activity on a trial-by-trial basis, where removal of non-timelocked activity through averaging (which we did when we tested for condition differences in Fig. 4 and 9) is not possible, there is uncertainty in the data. Baseline-correction can alleviate this issue, but it cannot offset the possibility of non-specific effects. We therefore decided to repeat the analysis with a fast-fourier calculated power instead of the Hilbert power, in favour of a higher and stricter frequency-resolution, as we averaged over a time-period and thus, the time-domain was not relevant for this analysis. In this more conservative analysis, we can see that only 36 Hz tagged activity when expecting an auditory target correlated with early visual alpha activity.

Additionally, we added correlation analyses between alpha activity and frequency-tagged activity within early visual areas, using the sensor cluster which showed significant condition differences in alpha activity. Here, no correlations between frequency-tagged activity and alpha activity could be found (apart from a small correlation with 40 Hz which could not be confirmed by a median split; see SUPPL Fig. 14 C). The absence of a significant correlation between early visual alpha and frequency-tagged activity has previously been described by others (Zhigalov & Jensen, 2020) and a Bayes factor of below 1 also indicated that the alternative hypotheses is unlikely.

Nonetheless, a correlation with auditory signal is possible and could be explained in different ways. For example, it could be that very early auditory feedback in early visual cortex (see for example Brang et al., 2022) is transmitted alongside visual information to higher-order areas. Several studies have shown that alpha activity and visual as well as auditory processing are closely linked together (Bauer et al., 2020; Popov et al., 2023). Inference on whether or how this link could play out in the case of this manuscript expands beyond the scope of this study.

To summarize, we believe the fact that 36 Hz activity within early visual areas does not correlate with alpha activity on a trial-by-trial basis, but that 36 Hz activity in other areas does, provides strong evidence that alpha activity affects down-stream signal processing.

We mention this analysis now in our discussion:

L533-536: Our data provides evidence in favour of this view, as we can show that early sensory alpha activity does not covary over trials with SSEP magnitude in early visual areas, but covaries instead over trials with SSEP magnitude in higher order sensory areas (see also SUPPL. Fig. 14).

Reviewer #1 (Recommendations for the authors):

The evidence for the alternative hypothesis, that alpha in early sensory areas orchestrates downstream signal transmission, is not strong enough to be described up front in the abstract and Figure 1. I would leave it in the Discussion section, but advise against mentioning it in the abstract and Figure 1.

We appreciate the reviewer’s concern regarding the inclusion of the alternative hypothesis—that alpha activity in early sensory areas orchestrates downstream signal transmission—in the abstract and Figure 1. While we agree that this interpretation is still developing, recent studies (Keitel et al., 2025; Clausner et al., 2024; Yang et al., 2024) provide growing support for this framework.

In response, we have revised the introduction, discussion, and Figure 1 to clarify that our intention is not to outright dismiss the alpha inhibition hypothesis, but to refine and expand it in light of new data. This revision does not invalidate the prior literature on alpha timing and inhibition; rather, it proposes an updated mechanism that may better account for observed effects.

We have though retained Figure 1, as it visually contextualizes the broader theoretical landscape. while at the same time added further analyses to strengthen our empirical support for this emerging view.

References:

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Author response:

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

Reviewer #1 (Public review): 

Summary: 

The paper by Boch and colleagues, entitled Comparative Neuroimaging of the Carnivore Brain: Neocortical Sulcal Anatomy, compares and describes the cortical sulci of eighteen carnivore species, and sets a benchmark for future work on comparative brains. 

Based on previous observations, electrophysiological, histological and neuroimaging studies and their own observations, the authors establish a correspondence between the cortical sulci and gyri of these species. The different folding patterns of all brain regions are detailed, put into perspective in relation to their phylogeny as well as their potential involvement in cortical area expansion and behavioral differences. 

Strengths: 

This is a pioneering article, very useful for comparative brain studies and conducted with great seriousness and based on many past studies. The article is well-written and very didactic. The different protocols for brain collection, perfusion, and scanning are very detailed. The images are self-explanatory and of high quality. The authors explain their choice of nomenclature and labels for sulci and gyri on all species, with many arguments. The opening on ecology and social behavior in the discussion is of great interest and helps to put into perspective the differences in folding found at the level of the different cortexes. In addition, the authors do not forget to put their results into the context of the laws of allometry. They explain, for example, that although the largest brains were the most folded and had the deepest folds in their dataset, they did not necessarily have unique sulci, unlike some of the smaller, smoother brains. 

Weaknesses: 

The article is aware of its limitations, not being able to take into account interindividual variability within each species, inter-hemispheric asymmetries, or differences between males and females. However, this does not detract from their aim, which is to lay the foundations for a correspondence between the brains of carnivores so that navigation within the brains of these species can be simplified for future studies. This article does not include comparisons of morphometric data such as sulci depth, sulci wall surface, or thickness of the cortical ribbon around the sulci. 

We thank the reviewer for their overwhelmingly positive evaluation of our work. As noted by the reviewer, our primary aim was to establish a framework for navigating carnivoran brains to lay the foundation for future research. We are pleased that this objective has been successfully achieved.

Individual differences

As the reviewer points out, we do not quantify within-species intraindividual differences, which was a conscious choice. We aimed to emphasise the breadth of species over individuals, as is standard in large-scale comparative anatomy (cf. Heuer et al., 2023, eLife; Suarez et al., 2022, eLife). Following the logic of phylogenetic relationships, the presence of a particular sulcus across related species is also a measure of reliability. We felt safe in this choice, as previous work in both primates and carnivorans has shown that differences across major sulci across individuals are a matter of degree rather than a case of presence or absence (Connolly, 1950, External morphology of the primate brain, C.C. Thomas; Hecht et al., 2019 J Neurosci; Kawamuro 1971 Acta Anat., Kawamuro & Naito, 1977, Acta Anat.). 

In our revised manuscript, we now include additional individuals for six different species, representing both carnivoran suborders (Feliformia and Caniformia), and within Caniformia, both Arctoidea and Canidae (see revised Table 1 and main changes in text below). These additions confirm that intra-species variation primarily affects sulcal shape rather than the presence or absence of major sulci. Furthermore, the inclusion of additional individuals helped validate some initial observations, for example, confirming that the brown bear's proreal sulcus is more accurately characterised as a branch of the presylvian sulcus.

Main changes in the revised manuscript:

Results and discussion, p. 13-14: Presylvian sulcus. Rostral to the pseudo-sylvian fissure, the perisylvian sulcus originates from or close to the rostral lateral rhinal fissure (see Supplementary Note 1 and Figure S2 for ventral view). The sulcus extends dorsally, and we observed a gentle caudal curve in the majority of the species (Figures 2-3, white).

There were no major variations across species, but we noted a shortened sulcus in the meerkat and Egyptian mongoose and the presence of a secondary branch at the dorsal end that extended rostrally in the Eurasian badger and South American coati brain. The brown bear exhibited an additional sulcus in the frontal lobe, previously labelled as the proreal sulcus (see, e.g., Sienkiewicz et al., 2019); however, its shape closely resembled the secondary branches of the perisylvian sulcus seen in the South American coati and Eurasian badger. Sienkiewicz et al. (2019) also noted that this sulcus merges with the presylvian sulcus in their specimen, consistent with our findings in the left hemisphere of the brown bear and bilaterally in the Ussuri brown bear (see Supplementary Figure S3A, S5A). Given the known gyrencephaly of Ursidae brains with frequent secondary and tertiary sulci (Lyras et al., 2023), we propose that this sulcus represents a branch of the perisylvian sulcus.

General Discussion, p. 23-24:Regarding individual variability in external brain morphology, previous work in primates and carnivorans has shown that differences across individuals typically affect sulcal shape, depth, or extent, but not the presence of major sulci. This has been reported in diverse contexts, including comparisons between captive and (semi-)wild macaque (Sallet et al., 2011; Testard et al., 2022), different dog breeds (Hecht et al., 2019), domestic cats (Kawamura, 1971b), or selectively bred foxes (Hecht et al., 2021). By including additional individuals for selected species, we extend these findings to a broader range of carnivorans. Notably, we observed no major sulcal differences between closely related species, even when specimens were acquired using different extraction and scanning protocols, for example, across felid clades or among wolf-like canids, further suggesting that substantial within-species variation is unlikely. While a full analysis of interindividual variability lies beyond the scope of this study, our findings support the reliability of the major sulcal patterns described.

Interhemispheric differences

Regarding potential inter-hemispheric differences, we have now also created digital atlases of all identified sulci in both hemispheres, which are publicly available at https://git.fmrib.ox.ac.uk/neuroecologylab/carnivore-surfaces. While the manuscript continues to focus primarily on descriptions of the right hemisphere, we now also report observed inter-hemispheric differences where applicable. These differences remain minor and, again, a matter of degree. For example, the complementary quantitative analyses investigating covariation between sulcal length and behavioural traits conducted in the right hemisphere were replicated in the left (Supplementary Figure S6 and related Supplementary tables S1-S3).

Main changes in the revised manuscript:  

Materials and Methods, p. 33: We focused on the major lateral and dorsal sulci of the carnivoran brain, but the medial wall and ventral view of the sulci are also described. For consistency, we started by labelling the right hemispheres on the mid-thickness surfaces; these are the hemispheres presented in the manuscript. An exception was made for the jungle cat, for which only the left hemisphere was available and is therefore shown. We aimed to facilitate interspecies comparisons and the exploration of previously undescribed carnivoran brains. To this end, we first created standardized criteria (henceforth referred to as recipes) for identifying each sulcus, drawing from existing literature on carnivoran neuroanatomy, particularly in paleoneurology (Lyras et al., 2023), and our own observations. In addition, we created digital sulcal masks for both hemispheres, which allowed us to test whether the same patterns were observable bilaterally and to further facilitate future research building on our framework. For the Egyptian mongoose, only the right hemisphere was available, and thus, a bilateral comparison was not possible for this species. Anatomical nomenclature primarily follows the recommendations of Czeibert et al (2018); if applicable, alternative names of sulci are provided once.

Materials and Methods, p. 34-35: We first briefly illustrated the gyri of the carnivoran brain with a focus on gyri that are not present in some species as a consequence of absent sulci to complement our observations. We then summarised the key differences and similarities in sulcal anatomy between species and related them to their ecology and behaviour. To complement this qualitative description, we conducted an initial quantitative analysis of sulcal length data from both hemispheres. 

To test whether sulcal length covaries with behavioural traits, we fit linear models predicting the relative length of the three target sulci (cruciate, postcruciate, proreal) as a function of forepaw dexterity (low vs.

high) and sociality (solitary vs cooperative hunting). We measured the absolute length of each sulcus using the wb_command -border-length function from the Connectome Workbench toolkit (Marcus et al., 2011) applied to the manually defined sulcal masks (i.e., border files). Relative sulcal length was calculated by dividing the length of each target sulcus by that of a reference sulcus in the same hemisphere, reducing interspecies variation in brain or sulcal size. Reference sulci were required to be present in all species within a hemisphere and excluded if they were a target sulcus, part of the same functional system (e.g., somatosensory/motor), or anatomically atypical (e.g., the pseudosylvian fissure). This resulted in seven reference sulci for the proreal sulcus (ansate, coronal, marginal, presylvian, retrosplenial, splenial, suprasylvian) and four for the cruciate and postcruciate sulci (marginal, retrosplenial, splenial, suprasylvian). For each target-reference pair, we fit the following linear model: relative length ~ forepaw dexterity + sociality. Models were run separately for left and right hemispheres, with the left serving as a replication test. Associations were considered meaningful if the predictor reached statistical significance (p ≤ .05) in ≥ 75% of reference sulcus models per hemisphere. Additional individuals were not included in the analysis.

Data and code availability statement, p. 35-36: Generated surfaces of all species and T1-like contrast images of post-mortem samples obtained by the C Generated surfaces of all species and T1-like contrast images of post-mortem samples obtained by the Copenhagen Zoo and the Zoological Society of London (see Table 1) are available at the Digital Brain Zoo of the University of Oxford (Tendler et al., 2022) (https://open.win.ox.ac.uk/DigitalBrainBank/#/datasets/zoo). For all other species, except the domestic cat, the cortical surface reconstructions are available through the same resource. In-vivo data for the domestic cat is available upon request.

We created, extracted and analysed sulcal length data using the Connectome Workbench toolkit (Marcus et al., 2011), R 4.4.0 (R Core Team, 2023) and Python 3.9.7. Sulcal masks, along with the associated midthickness cortical surface reconstructions for all 32 animals, species-specific behavioural data, and the code used to extract sulcal lengths and perform the statistical analyses are available at: https://git.fmrib.ox.ac.uk/neuroecologylab/carnivore-surfaces. 

Further brain measures

We feel that sulci depth, sulci wall surface, or thickness of the cortical ribbon are measures that vary more across individuals, and we have therefore not included them in the study. In addition, these are measures that are not generally used as betweenspecies comparative measures, whereas sulcal patterning is (cf. Amiez et al., 2019, Nat Comms; Connolly, 1950; Miller et al., 2021, Brain Behav Evol; Radinsky 1975, J Mammal; Radinsky 1969, Ann N Y Acad Sci; Welker & Campos 1963 J. Comp Neurol).

We, therefore, added them as suggestions for future directions, building on our work.

Major changes in the revised manuscript:

Limitations and future directions, p. 25-26: Our findings represent a critical first step for linking brains within and across species for interspecies insights. The present analyses are based on multiple individuals pooled into families and genera, primarily focusing on single representatives per species. Additional individuals for selected species confirmed that intra-species variation is a matter of degree rather than a case of presence or absence of major sulci, but we do not provide an extensive account of the possible range of sulcal shape or other anatomical features. Future studies will aim to systematically investigate interindividual variability in sulcal shape, depth, surface area, or thickness of the cortical ribbon surrounding the sulci, and will extend to more detailed investigations of the medial part of the cortex, as well as the subcortical structures and the cerebellum.The present framework and resulting database also provides the foundation to guide and facilitate future investigations of inter- and intra-species variation in regional brain size.

Reviewer #2 (Public review): 

Summary: 

The authors have completed MRI-based descriptions of the sulcal anatomy of 18 carnivoran species that vary greatly in behaviour and ecology. In this descriptive study, different sulcal patterns are identified in relation to phylogeny and, to some extent, behaviour. The authors argue that the reported differences across families reflect behaviour and electrophysiology, but these correlations are not supported by any analyses. 

Strengths: 

A major strength of this paper is using very similar imaging methods across all specimens. Often papers like this rely on highly variable methods so that consistency reduces some of the variability that can arise due to methodology. 

The descriptive anatomy was accurate and precise. I could readily follow exactly where on the cortical surface the authors referring. This is not always the case for descriptive anatomy papers, so I appreciated the efforts the authors took to make the results understandable for a broader audience. 

I also greatly appreciate the authors making the images open access through their website. 

Weaknesses: 

Although I enjoyed many aspects of this manuscript, it is lacking in any quantitative analyses that would provide more insights into what these variations in sulcal anatomy might mean. The authors do discuss inter-clade differences in relation to behaviour and older electrophysiology papers by Welker, Campos, Johnson, and others, but it would be more biologically relevant to try to calculate surface areas or volumes of cortical fields defined by some of these sulci. For example, something like the endocast surface area measurements used by Sakai and colleagues would allow the authors to test for differences among clades, in relation to brain/body size, or behaviour. Quantitative measurements would also aid significantly in supporting some of the potential correlations hinted at in the Discussion.  

Although quantitative measurements would be helpful, there are also some significant concerns in relation to the specimens themselves. First, almost all of these are captive individuals. We know that environmental differences can alter neocortical development and humans and nonhuman animals and domestication affects neocortical volume and morphology. Whether captive breeding affects neocortical anatomy might not be known, but it can affect other brain regions and overall brain size and could affect sulcal patterns. Second, despite using similar imaging methods across specimens, fixation varied markedly across specimens. Fixation is unlikely to affect the ability to recognize deep sulci, but variations in shrinkage could nevertheless affect overall brain size and morphology, including the ability to recognize shallow sulci. Third, the sample size = 1 for every species examined. In humans and nonhuman animals, sulcal patterns can vary significantly among individuals. In domestic dogs, it can even vary greatly across breeds. It, therefore, remains unclear to what extent the pattern observed in one individual can be generalized for a species, let alone an entire genus or family. The lack of accounting for inter-individual variability makes it difficult to make any firm conclusions regarding the functional relevance of sulcal patterns. 

We thank the reviewer for their assessment of our work. The primary aim of this study was to establish a framework for navigating carnivoran brains by providing a comprehensive overview of all major neocortical sulci across eighteen different species. Given the inconsistent nomenclature in the literature and the lack of standardized criteria (“recipes”) for identifying the major sulci, we specifically focused on homogenizing the terminology and creating recipes for their identification. In addition to generating digital cortical surfaces for all brains, we have now also added sulcal masks to further support future research building on this framework. We are pleased that our primary objective is seen as successfully achieved and are delighted to report that, following the reviewer’s recommendations, we have further expanded the dataset by including eight additional species and a second individual for six species, yielding a total of 32 carnivorans from eight carnivoran families (see revised Table 1 for a detailed list).

The present dataset constitutes the most comprehensive collection of fissiped carnivoran brains to date, encompassing a wide range of land-dwelling species from eight families. It includes diverse representatives, such as both social and solitary mongooses, weasel-like and non-weasel mustelids, and a broad spectrum of canids including wolf-like, fox-like, and more basal forms. Further expanding this already extensive dataset has even led to novel discoveries, such as the felid-specific diagonal sulcus and the unique occipito-temporal sulcal configuration shared by herpestids and hyaenids. 

Major changes in the revised manuscript:

Results and discussion, p. 4-5: We labelled the neocortical sulci of twenty-six carnivoran species (see Figure 1) based on reconstructed surfaces and developed standardised criteria (“recipes”) for identifying each major sulcus. For each sulcus, we also created corresponding digital masks. Our study included eleven Feliformia and fifteen Caniformia species from eight different carnivoran families. Within the suborder Caniformia, we examined eight Canidae and seven Arctoidea species. In addition, we describe relative intra-species variation in sulcal shape based on supplementary specimens from six species (see Table 1).

Overall, of the carnivorans studied, Canidae brains exhibited the largest number of unique major sulci, while the brown bear brain was the most gyrencephalic, with the deepest folds and many secondary sulci (see Figures 2-3; brains are arranged by descending number of major sulci). The brown bear was also the largest animal in the sample. The brains of the smaller species, such as the fennec fox, meerkat or ferret, were the most lissencephalic, with the sulci having fewer undulations or indentations compared to the other species. A similar trend has also been observed in the sulci of the prefrontal cortex in primates (Amiez et al., 2023, 2019). The meerkat and Egyptian mongoose exhibited the smallest number of major sulci but possessed, along with the striped hyena, a unique configuration of sulci in the occipito-temporal cortex. In the following, we describe each sulcus' appearance, the recipes on how to identify them, and provide an overview of the most significant differences across species.

Results and discussion, p. 11: Diagonal sulcus. The diagonal sulcus is oriented nearly perpendicularly to the rostral portion of the suprasylvian sulcus (Figure 2, Supplementary Figure S2, red). We identified it in all Felidae and in the striped hyena, but it was absent in Herpestidae and all Caniformia species.

In our sample, the sulcus showed moderate variation in shape and continuity. In the caracal and the second sand cat, it appeared as a detached continuation of the rostral suprasylvian sulcus (Supplementary Figure S3). In the Amur and Persian leopards, the diagonal sulcus merged with the rostral ectosylvian sulcus on the right hemisphere, forming a continuous or bifurcated groove. Similar individual variation has been described in domestic cats (Kawamura, 1971b).

We respectfully disagree with the reviewer on two accounts, where we believe the revieweris not judging the scope of the current work

(1) Intra-individual differences & potential confounding factors

The first is with respect to individual differences relationships. To the best of our knowledge, differences between captive and wild animals, or indeed between individuals, do not affect the presence or absence of any major sulci. No differences in sulcal patterns were detected between captive and (semi-)wild macaques (cf. Sallet et al., 2011, Science; Testard et al., 2022, Sci Adv), different dog breeds (Hecht et al., 2019 J Neurosci) or foxes selectively bred to simulate domestication, compared to controls (Hecht et al., 2021 J. Neurosci). 

By including additional individuals for selected species in the revised version of our manuscript, we confirm and extend these findings to a broader range of carnivorans. Indeed, we also did not observe major differences between closely related species, even when specimens were collected using different extraction and scanning protocols - for example, across felid clades or wolf-like canids - making substantial individual variation within a species even less likely. Thus, while a comprehensive analysis of interindividual variability is beyond the scope of this study, our observations support the robustness of the major sulcal patterns described here. Moreover, the inclusion of additional individuals also helped validate some initial observations, for example, confirming that the brown bear's proreal sulcus is more accurately characterised as a branch of the presylvian sulcus.

We do, however, agree with the reviewer that building up a database like ours benefits from providing as much information about the samples as possible to enable these issues to be tested. We, therefore, made sure to include as detailed information as possible, including whether the animals were from captive or wild populations, in our manuscript. 

Main changes in the revised manuscript: 

Results and discussion, p. 13-14: Presylvian sulcus. There were no major variations across species, but we noted a shortened sulcus in the meerkat and Egyptian mongoose and the presence of a secondary branch at the dorsal end that extended rostrally in the Eurasian badger and South American coati brain. The brown bear exhibited an additional sulcus in the frontal lobe, previously labelled as the proreal sulcus (see, e.g., Sienkiewicz et al., 2019); however, its shape closely resembled the secondary branches of the perisylvian sulcus seen in the South American coati and Eurasian badger. Sienkiewicz et al. (2019) also noted that this sulcus merges with the presylvian sulcus in their specimen, consistent with our findings in the left hemisphere of the brown bear and bilaterally in the Ussuri brown bear (see Supplementary Figure S3A, S5A). Given the known gyrencephaly of Ursidae brains with frequent secondary and tertiary sulci (Lyras et al., 2023), we propose that this sulcus represents a branch of the perisylvian sulcus.

Results and discussion, p. 23-24: Regarding individual variability in external brain morphology, previous work in primates and carnivorans has shown that differences across individuals typically affect sulcal shape, depth, or extent, but not the presence of major sulci. This has been reported in diverse contexts, including comparisons between captive and (semi-)wild macaque (Sallet et al., 2011; Testard et al., 2022), different dog breeds (Hecht et al., 2019), domestic cats (Kawamura, 1971b), or selectively bred foxes (Hecht et al., 2021). By including additional individuals for selected species, we extend these findings to a broader range of carnivorans. Notably, we observed no major sulcal differences between closely related species, even when specimens were acquired using different extraction and scanning protocols, for example, across felid clades or among wolf-like canids, further suggesting that substantial within-species variation is unlikely. While a full analysis of interindividual variability lies beyond the scope of this study, our findings support the reliability of the major sulcal patterns described.

Limitations and future directions, p. 25-26: Our findings represent a critical first step for linking brains within and across species for interspecies insights. The present analyses are based on multiple individuals pooled into families and genera, primarily focusing on single representatives per species. Additional individuals for selected species confirmed that intra-species variation is a matter of degree rather than a case of presence or absence of major sulci, but we do not provide an extensive account of the possible range of sulcal shape or other anatomical features.

Future studies will aim to systematically investigate interindividual variability in sulcal shape, depth, surface area, or thickness of the cortical ribbon surrounding the sulci, and will extend to more detailed investigations of the medial part of the cortex, as well as the subcortical structures and the cerebellum.The present framework and resulting database also provides the foundation to guide and facilitate future investigations of inter- and intra-species variation in regional brain size.

(2) Quantification of structure/function relationships

The second is in the quantification of structure/function relationships. We believe the cortical surfaces, detailed sulci descriptions, and atlases themselves are the main deliverables of this project. We felt it prudent to include some qualitative descriptions of the relationship between sulci as we observed them and behaviours as known from the literature, as a way to illustrate the possibilities that this foundational work opens up. This approach also allowed us to confirm and extend previous findings based on observations from a less diverse range of carnivoran species and families (Radinsky 1968 J Comp Neurol; Radinsky 1969, Ann N Y Acad Sci; Welker & Campos 1963 J Comp Neurol; Welker & Seidenstein, 1959 J Comp Neurol).

However, a full statistical framework for analysis is beyond the scope of this paper. Our group has previously worked on methods to quantitatively compare brain organization across species - indeed, we have developed a full framework for doing so (Mars et al., 2021, Annu Rev Neurosci), based on the idea that brains that differ in size and morphology should be compared based on anatomical features in a common feature space. Previously, we have used white matter anatomy (Mars et al., 2018, eLife) and spatial transcriptomics (Beauchamp et al., 2021, eLife). The present work presents the foundation for this approach to be expanded to sulcal anatomy, but the full development of it will be the topic of future communications.

Nevertheless, we now include a preliminary quantitative analysis of the relationship between the relative length of specific sulci and the two behavioural traits of interest. These analyses, which complement the qualitative observations in Figure 5, show that the relative length of the proreal sulcus was consistently greater in highly social, cooperatively hunting species, while no effect of forepaw dexterity was found (Supplementary Table S1). In contrast, both the cruciate and postcruciate sulci were significantly longer in species with high forepaw dexterity, but not related to sociality (Supplementary Tables S2–S3). These findings were consistent across reference sulci used to compute relative sulcal length and replicated in the left hemisphere (see Supplementary Figure S6).

We also would like to emphasize that we strongly believe that looking at measures of brain organization at a more detailed level than brain size or relative brain size is informative. Although studies correlating brain size with behavioural variables are prominent in the literature, they often struggle to distinguish between competing behavioural hypotheses (Healy, 2021, Adaptation and the Brain, OUP). In contrast, connectivity has a much more direct relationship to behavioural differences across species (Bryant et al., 2024, JoN), as does sulcal anatomy (Amiez et al., 2019, Nat Comms; Miller et al., 2021, Brain Behav Evol). Using our sulcal framework, we observed lineage-specific variations that would be overlooked by analyses focused solely on brain size. Moreover, such measures are less sensitive to the effects of fixation since that will affect brain size but not the presence or absence of a sulcus.

Main changes in the revised manuscript:

Results and discussion, p. 16-17: In the raccoon, red panda, coati, and ferret, considerably larger portions of the postcruciate gyrus S1 area appeared to be allocated to representing the forepaw and forelimbs (McLaughlin et al., 1998; Welker and Campos, 1963; Welker and Seidenstein, 1959) when compared to the domestic cat or dog (Dykes et al., 1980; Pinto Hamuy et al., 1956). This aligns with the observation that all species in the present sample with more complex or elongated postcruciate and cruciate sulci configurations display a preference for using their forepaws when manipulating their environment (see e.g., Iwaniuk et al., 1999; Iwaniuk and Whishaw, 1999; Radinsky, 1968; and Figure 5A). Complementary quantitative analyses further support this link, revealing a positive relationship between the relative length of the cruciate and postcruciate sulci and high forepaw dexterity (see Supplementary Figure S6, Tables S2-S3). This is suggestive of a potential link between sulcal morphology and a behavioural specialization in Arctoidea, consistent with earlier observations in otter species (Radinsky, 1968). 

Results and discussion, p. 21: A distinct proreal sulcus was observed in the frontal lobe of the domestic dog, the African wild dog, wolf, dingo, and bush dog. This may indicate an expansion of frontal cortex in these animals compared to the other species in our sample (Figure 5-6). This aligns with findings from a comprehensive study comparing canid endocasts revealing an expanded proreal gyrus in these animals compared to the fennec fox, red fox and other species of the genus Vulpes (Lyras and Van Der Geer, 2003). The canids with a proreal sulcus also exhibit complex social structures compared to the primarily solitary living foxes (Nowak, 2005; Wilson and Mittermeier, 2009; Wilson, 2000, and see Figure 5).Despite living in social groups, the bat-eared fox, an insectivorous canid, does not possess a proreal sulcus. Its foraging behaviour is best described as spatially or communally coordinated rather than truly cooperative (Macdonald and Sillero-Zubiri, 2004), suggesting that the relationship between sulcal morphology and sociality may be specific to species engaging in active cooperative hunting. Supplementary quantitative analyses also confirm an increase in the relative length of the proreal sulcus

in cooperatively hunting species Moreover, a previous investigation of Canidae and Felidae brain evolution, using endocasts of extant and extinct species, also suggested a link between the emergence of pack structures and the proreal sulcus in Canidae (Radinsky, 1969). Despite being highly social and living in large social groups (i.e., mobs), meerkats appear to have a relatively small frontal lobe and no proreal sulcus compared to the social Canids (Figure 5), which would suggest that if the presence of a proreal sulcus correlates with complex social behaviour, this is canid-specific.

General discussion, p. 22-23: Our results revealed several interesting patterns of local variation in sulcal morphology between and within different lineages, and successfully replicate and expand upon prior observations based on more limited sets of species (Radinsky, 1969, 1968; Welker and Campos, 1963; Welker and Seidenstein, 1959). For example, Arctoidea showed relatively complex sulcal anatomy in the somatosensory cortex but low complexity in the occipito-temporal regions. In Canidae and Felidae, we found more complex occipito-temporal sulcal patterns indicative of changes in the amount of cortex devoted to visual and auditory processing in these regions. These observations may be linked to social or ecological factors, such as how the animals interact with objects or each other and their varied foraging strategies. Another example was the differential relative expansion of the neocortex surrounding the cruciate sulcus, which was particularly complex in Arctoidea species that are known to use their paws to manipulate their environment. Consistent with this observation, complementary quantitative analyses of both hemispheres revealed that species with high forepaw dexterity tended to have longer cruciate and postcruciate sulci. Although it has been argued that the cruciate sulcus appeared independently in different lineages and its exact relationship to the location of primary motor areas varies (Radinsky, 1971), our results provide a detailed exploration of the relationship between brain morphology and behavioural preferences across such a range of species.  

Materials and Methods, p. 33: We focused on the major lateral and dorsal sulci of the carnivoran brain, but the medial wall and ventral view of the sulci are also described. For consistency, we started by labelling the right hemispheres on the mid-thickness surfaces; these are the hemispheres presented in the manuscript. An exception was made for the jungle cat, for which only the left hemisphere was available and is therefore shown. We aimed to facilitate interspecies comparisons and the exploration of previously undescribed carnivoran brains. To this end, we first created standardized criteria (henceforth referred to as recipes) for identifying each sulcus, drawing from existing literature on carnivoran neuroanatomy, particularly in paleoneurology (Lyras et al., 2023), and our own observations.In addition, we created digital sulcal masks for both hemispheres, which allowed us to test whether the same patterns were observable bilaterally and to further facilitate future research building on our framework. For the Egyptian mongoose, only the right hemisphere was available, and thus, a bilateral comparison was not possible for this species. Anatomical nomenclature primarily follows the recommendations of Czeibert et al (2018); if applicable, alternative names of sulci are provided once.

Materials and Methods, p. 34-35: We first briefly illustrated the gyri of the carnivoran brain with a focus on gyri that are not present in some species as a consequence of absent sulci to complement our observations. We then summarised the key differences and similarities in sulcal anatomy between species and related them to their ecology and behaviour. To complement this qualitative description, we conducted an initial quantitative analysis of sulcal length data from both hemispheres.  To test whether sulcal length covaries with behavioural traits, we fit linear models predicting the relative length of the three target sulci (cruciate, postcruciate, proreal) as a function of forepaw dexterity (low vs.high) and sociality (solitary vs cooperative hunting). We measured the absolute length of each sulcus using the wb_command -border-length function from the Connectome Workbench toolkit (Marcus et al., 2011) applied to the manually defined sulcal masks (i.e., border files). Relative sulcal length was calculated by dividing the length of each target sulcus by that of a reference sulcus in the same hemisphere, reducing interspecies variation in brain or sulcal size. Reference sulci were required to be present in all species within a hemisphere and excluded if they were a target sulcus, part of the same functional system (e.g., somatosensory/motor), or anatomically atypical (e.g., the pseudosylvian fissure). This resulted in seven reference sulci for the proreal sulcus (ansate, coronal, marginal, presylvian, retrosplenial, splenial, suprasylvian) and four for the cruciate and postcruciate sulci (marginal, retrosplenial, splenial, suprasylvian). For each target-reference pair, we fit the following linear model: relative length ~ forepaw dexterity + sociality. Models were run separately for left and right hemispheres, with the left serving as a replication test. Associations were considered meaningful if the predictor reached statistical significance (p ≤ .05) in ≥ 75% of reference sulcus models per hemisphere. Additional individuals were not included in the analysis.

Data and code availability statement, p. 35-36: Generated surfaces of all species and T1-like contrast images of post-mortem samples obtained by the C Generated surfaces of all species and T1-like contrast images of post-mortem samples obtained by the Copenhagen Zoo and the Zoological Society of London (see Table 1) are available at the Digital Brain Zoo of the University of Oxford (Tendler et al., 2022) (https://open.win.ox.ac.uk/DigitalBrainBank/#/datasets/zoo). For all other species, except the domestic cat, the cortical surface reconstructions are available through the same resource. In-vivo data for the domestic cat is available upon request.

We created, extracted and analysed sulcal length data using the Connectome Workbench toolkit (Marcus et al., 2011), R 4.4.0 (R Core Team, 2023) and Python 3.9.7. Sulcal masks, along with the associated midthickness cortical surface reconstructions for all 32 animals, species-specific behavioural data, and the code used to extract sulcal lengths and perform the statistical analyses are available at:

https://git.fmrib.ox.ac.uk/neuroecologylab/carnivore-surfaces. 

Reviewer #1 (Recommendations for the authors): 

I was convinced by your model of labels in the temporal region and the nomenclature used, thanks to your argument concerning the primary auditory area in ferrets located in the gyrus called ectosylvian even though they have no ectosylvian sulcus. While this region raises questions, it seems to me that you make a good case for your labelling. 

However, I don't understand your arguments in the occipital region regarding the ectomarginal sulcus. In the bear, for example, I don't understand why the caudal part of the marginal sulcus is not referred to as ectomarginal? You say that this sulci is specific to canids.

Whether in the paragraph describing the ectomarginal sulcus, the marginal sulcus, in the paragraphs on the gyri, or in the paragraph concerning the potential relationship to function, I don't see any argument to support your hypothesis. Especially as there is no information in the literature on the functions in this area of the bear brain as in that of the dog or other related species. 

You just mention that in Canidae, the ectomarginal "runs between the suprasylvian and marginal sulcus", and I don't see why this is an argument. 

Could you explain in more detail your choice of label and the specificity you claim to have in the canids of this region? 

We have now expanded our rationale in the revised manuscript, particularly in the section describing the marginal sulcus, which directly follows the description of the ectomarginal sulcus. In brief, across our sample, including Ursidae and Canidae, we observed variation in whether the caudal marginal sulcus was detached or continuous, or extended further caudally vs ventrally, but no separate additional sulcus resembling the ectomarginal sulcus was seen in any species outside the canid family. We therefore reserve the label ectomarginal sulcus for the distinct structure consistently observed in Canidae and avoid applying it to the detached caudal marginal sulcus observed in Ursidae.

Main changes in the revised manuscript:

Results and discussion, p. 10-11: In several species, including the dingo, domestic cat, brown bear and South American coati and further supplementary individuals (Supplementary figure S3B), the caudal portion of the marginal sulcus was detached in one or both hemispheres, which is a frequently reported occurrence (England, 1973; Kawamura, 1971a; Kawamura and Naito, 1978). Potentially due to the similar caudal bend, some authors have labelled the (detached) caudal portion of the marginal sulcus in Ursidae as the ectomarginal sulcus (Lyras et al., 2023, but see e.g., Sienkiewicz et al., 2019); 

The (detached) caudal marginal sulcus in Ursidae continues the course of the marginal sulcus caudally and/or ventrally and is topologically continuous with it. In contrast, the ectomarginal sulcus in Canidae is an entirely separate sulcus that runs between the suprasylvian and marginal sulci, forming a small, additional arch that is rarely connected to the marginal sulcus (Kawamura and Naito, 1978). This distinction is illustrated, for example, in the dingo and grey wolf. In the dingo, we observed both a detached caudal extension of the marginal sulcus and a distinct ectomarginal sulcus. In both grey wolf specimens, the marginal sulcus extended ventrally in a way that resembled the brown bear, but they also exhibited a clearly separate ectomarginal sulcus, confirming that the two features are not equivalent. In contrast, in the brown bear and Ussuri brown bear (Supplementary Figure S3B), we observed variation in whether the marginal sulcus was detached or continuous, but no separate sulcus resembling the ectomarginal sulcus seen in Canidae.

Reviewer #2 (Recommendations for the authors): 

Although I indicated this already, I stress that the lack of quantification is problematic. In its current format, this is a classic descriptive study suitable for an anatomy journal, but even then, the conclusions are highly speculative. I would advise including some quantification of sulcal lengths or depths and surface areas or volumes of individual regions and relate all of those to overall brain size and potential clade differences. Figure 5 hints at some of these putative correlations, but is not an analysis. Some of these correlations are discussed in the manuscript, but without quantification, it is simply more descriptions and some speculative associations that largely parallel and corroborate findings from Radinsky's papers.  In addition to quantification, the authors should consider a more fulsome explanation of the potential confounds and limitations of their data. As alluded to above, there are many sources of variation that were not sufficiently discussed but are critically important for interpreting any putative differences among and within clades.  

We would like to reiterate that the primary aim of our study was to establish a comprehensive sulcal framework for carnivoran brains. The behavioural and ecological associations were secondary and exploratory, arising from a first application of this framework, and will require further investigation in future studies. 

We already acknowledged in the initial version of the manuscript that many of our observations were consistent with those previously reported by Radinsky in more limited sets of species. However, we recognise that this point may not have come across clearly. We carefully revised our manuscript to further emphasise that our findings replicate and extend Radinsky’s work in a larger cross-species comparison, showing that our framework also successfully replicates and expands prior work. 

As detailed in the public reviews, we did not measure overall or relative brain sizes. However, in the revised version of the manuscript, we have now quantified the relationship between sulcal length and its association with forepaw dexterity and sociality to complement the qualitative observations in Figure 5. Although preliminary, we believe that these analyses further showcase the strength of our sulcal framework and its potential for future investigations. 

We also revised our discussion section to highlight the potential for future studies to build on our framework to systematically investigate interindividual variability in sulcal shape, depth, surface area, or thickness of the cortical ribbon surrounding the sulci. We also added that our framework and accompanying dataset can facilitate and guide future investigations into both inter- and intra-species variation in regional brain size.

Main changes in the revised manuscript:

General discussion, p. 22-23: Our results revealed several interesting patterns of local variation in sulcal morphology between and within different lineages, and successfully replicate and expand upon prior observations based on more limited sets of species (Radinsky, 1969, 1968; Welker and Campos, 1963; Welker and Seidenstein, 1959). For example, Arctoidea showed relatively complex sulcal anatomy in the somatosensory cortex but low complexity in the occipito-temporal regions. In Canidae and Felidae, we found more complex occipito-temporal sulcal patterns indicative of changes in the amount of cortex devoted to visual and auditory processing in these regions. These observations may be linked to social or ecological factors, such as how the animals interact with objects or each other and their varied foraging strategies. Another example was the differential relative expansion of the neocortex surrounding the cruciate sulcus, which was particularly complex in Arctoidea species that are known to use their paws to manipulate their environment. Consistent with this observation, complementary quantitative analyses of both hemispheres revealed that species with high forepaw dexterity tended to have longer cruciate and postcruciate sulci. Although it has been argued that the cruciate sulcus appeared independently in different lineages and its exact relationship to the location of primary motor areas varies (Radinsky, 1971), our results provide a detailed exploration of the relationship between brain morphology and behavioural preferences across such a range of species.

Limitations and future directions, p. 25-26: Our findings represent a critical first step for linking brains within and across species for interspecies insights. The present analyses are based on multiple individuals pooled into families and genera, primarily focusing on single representatives per species. Additional individuals for selected species confirmed that intra-species variation is a matter of degree rather than a case of presence or absence of major sulci, but we do not provide an extensive account of the possible range of sulcal shape or other anatomical features. Future studies will aim to systematically investigate interindividual variability in sulcal shape, depth, surface area, or thickness of the cortical ribbon surrounding the sulci, and will extend to more detailed investigations of the medial part of the cortex, as well as the subcortical structures and the cerebellum. The present framework and resulting database also provides the foundation to guide and facilitate future investigations of inter- and intra-species variation in regional brain size.

Another point that I did not see raised in the Discussion, but would be important and useful to include is that the authors are lacking specimens for several clades that could show additional differences in neocortical anatomy. For example, no hyaenids or viverrids were represented and an otter and badger are not necessarily representative of all mustelids, the majority of which are weasel-like. One could even argue that the meerkat is not necessarily representative of all herpestids given its behaviour and ecology. Of course, there are also pinnipeds, but they are divergent in many ways, and restricting the analyses to fissiped carnivorans is completely reasonable. Please note that I am not suggesting that the authors go back and try to procure even more species; rather they should emphasize that this is an incomplete survey of fissiped carnivorans. 

The reviewer’s comments prompted us to further expand our carnivoran brain collection to include a broader range of species, representatives, and individual specimens. Notably, the collection now includes a hyaenid representative, the striped hyena. In addition to the otter and badger, we have added a weasel-like mustelid, the ferret, as well as the solitary Egyptian mongoose to complement the highly social meerkat within Herpestidae. Our felid dataset has also been expanded to include additional small and large wild cats, such as the sand cat and the Bengal tiger. As described above, these additions have led to the discovery of novel sulcal patterns, including the felid-specific diagonal sulcus.

We now also specify the fissiped families currently missing from the collection, which can be readily incorporated using our existing sulcal framework. The same applies to pinniped species, which we are currently investigating to support broader macro-level comparisons across the order. 

Main changes in the revised manuscript:

General discussion, p. 23: Comparative neuroimaging requires balancing the level of anatomical detail with the breadth of species. The present sample represents the most comprehensive collection of fissiped carnivoran brains to date, encompassing a wide range of land-dwelling species from eight families. It includes diverse representatives, such as both social and solitary mongooses, weasel-like and non-weasel mustelids, and a broad array of canids, including wolf-like, fox-like, and more basal forms of canids. The framework and detailed protocols developed in this study are designed to facilitate navigation of additional fissiped species, such as Viverridae, Eupleridae, Mephitidae, Nandiniidae, and

Prionodontidae. Moreover, the approach can be readily extended to aquatic carnivorans, enabling broader macro-level comparisons across the order.

Apart from these broader issues, I also found some of the figures difficult to interpret in many instances. For example, the colour scheme used to highlight sulci is not colourblind friendly for Figures 2 and 3. It was also difficult for me to glean much information from Figure 6. I understand that functional regions of the cortex are shown for those species that were subject to electrophysiological studies in the past, but I could not work out how to transfer that data to the other brains. One suggestion for improving this would be to highlight putative cortical regions on the other brains in a lighter shade of the same colours. 

We have carefully revised our figures to improve clarity and accessibility, particularly for individuals with colour vision deficiencies. Specifically, we have added numerical labels alongside the coloured sulci labels in Figures 2 and 3, as well as in all related supplementary figures (see examples on the following pages). For sulci that merge, such as the marginal, ansate, and coronal sulci, we have used colour combinations that are distinguishable across all major types of colour-blindness. Figure 4 has also been updated with a colour-blind-friendly palette and additional numerical labels for the gyri to further enhance interpretability.

Regarding Figure 6, we have updated the colour palette to ensure accessibility and have labelled all landmark sulci discussed in the main text using acronyms (e.g., the postcruciate sulcus as the boundary between S1 and M1). This is intended to facilitate the transfer of information between brains and guide orientation for readers less familiar with these structures. While we appreciate the suggestion to highlight putative cortical regions on other brains, we have opted not to do so. Our concern is that such visual cues, even when rendered in lighter shades, may be misinterpreted as established rather than hypothetical regional boundaries. We believe this more conservative approach appropriately reflects the current evidence base and avoids unintentionally overstating the certainty of functional homologies.

Author response:

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

Reviewer #1 (Public review):

Summary:

Recruitment of neutrophils to the lungs is known to drive susceptibility to infection with M. tuberculosis. In this study, the authors present data in support of the hypothesis that neutrophil production of the cytokine IL-17 underlies the detrimental effect of neutrophils on disease. They claim that neutrophils harbor a large fraction of Mtb during infection, and are a major source of IL-17. To explore the effects of blocking IL-17 signaling during primary infection, they use IL-17 blocking antibodies, SR221 (an inverse agonist of Th17 differentiation), and celecoxib, which they claim blocks Th17 differentiation, and observe modest improvements in bacterial burdens in both WT and IFN-γ deficient mice using the combination of IL-17 blockade with celecoxib during primary infection. Celecoxib enhances control of infection after BCG vaccination.

Thank you for the summary.

Strengths:

The most novel finding in the paper is that treatment with celecoxib significantly enhances control of infection in BCG-vaccinated mice that have been challenged with Mtb. It was already known that NSAID treatments can improve primary infection with Mtb.

Thank you.

Weaknesses:

The major claim of the manuscript - that neutrophils produce IL-17 that is detrimental to the host - is not strongly supported by the data. Data demonstrating neutrophil production of IL17 lacks rigor. 

Our response: Neutrophil production of IL-17 is supported by two independent methods/ techniques in the current version: 

(1) Through Flow cytometry- a large fraction of Ly6G⁺CD11b⁺ cells from the lungs of Mtb-infected mice were also positive for IL-17 (Fig. 3C).

(2) IFA co-staining of Ly6G <SUP>+</SUP> cells with IL-17 in the lung sections from Mtb-infected mice (Fig. 3 E_G and Fig. 4H, Fig. 5I). For most of these IFA data, we provide quantified plots to show IL17<SUP>+</SUP>Ly6G<SUP>+</SUP> cells.

(3) Most importantly, conditions that inhibited IL-17 levels and controlled infection also showed a decline in IL-17 staining in Ly6G<SUP>+</SUP> cells.

Our efforts on IL-17 ELISPOT assay were not very successful and it needs further standardization. 

Several independent publications support the production of IL-17 by neutrophils (Li et al. 2010; Katayama et al. 2013; Lin et al. 2011). For example, neutrophils have been identified as a source of IL-17 in human psoriatic lesions (Lin et al. 2011), in neuroinflammation induced by traumatic brain injury (Xu et al. 2023) and in several mouse models of infectious and autoimmune inflammation (Ferretti et al. 2003; Hoshino et al. 2008) (Li et al. 2010).

The experiments examining the effects of inhibitors of IL-17 on the outcome of infection are very difficult to interpret. First, treatment with IL-17 inhibitors alone has no impact on bacterial burdens in the lung, either in WT or IFN-γ KO mice. This suggests that IL-17 does not play a detrimental role during infection. Modest effects are observed using the combination of IL-17 blocking drugs and celecoxib, however, the interpretation of these results mechanistically is complicated. Celecoxib is not a specific inhibitor of Th17. Indeed, it affects levels of PGE2, which is known to have numerous impacts on Mtb infection separate from any effect on IL-17 production, as well as other eicosanoids. 

The reviewer correctly says that Celecoxib is not a specific inhibitor of Th17. However, COX2 inhibition does have an effect on IL-17 levels, and numerous reports support this observation (Paulissen et al. 2013; Napolitani et al. 2009; Lemos et al. 2009).

(1) The detrimental role of IL-17 is obvious in the IFNγ KO experiment, where IL-17 neutralization led to a significant improvement in the lung pathology.

(2) In the highly susceptible IFNγ KO mice, IL-17 neutralization alone extended the survival of mice by ~10 days.

(3) IL-17 production independent of IL-23 is known to require PGE2 (Paulissen et al. 2013; Polese et al. 2021). In either WT or IFNγ KO mice, in contrast to IL-17 levels, we observed a decline in IL-23 levels. The PGE2 dependence of IL-17 production is obvious in the WT mice, where celecoxib abrogated IL-17 production.

(4) While deciding the impact of celecoxib or IL17 inhibition, looking at the cumulative readout of lung CFU, spleen CFU, Ly6G⁺ cell recruitment, Ly6G⁺ cell-resident Mtb pool and overall pathology, the effects are quite significant.

(5) Finally, in the revised manuscript, we provide additional results on the effect of SR2211 in BCG-vaccinated animals. It shows the direct impact of IL-17 inhibition on the BCG vaccine efficacy in WT mice.

Finally, the human data simply demonstrates that neutrophils and IL-17 both are higher in patients who experience relapse after treatment for TB, which is expected and does not support their specific hypothesis. 

We disagree with the above statement. It also contradicts reviewers’ own assessments in one of the comments below, where a protective role of IL-17 is referred to. The literature lacks consensus in terms of a protective or pathological role of IL-17 in TB. Therefore, it was not expected to see higher IL-17 in patients who experienced relapse, death, or failed treatment outcomes. We do not have evidence from human subjects whether neutrophil-derived IL-17 has a similar pathological role as observed in mice. However, higher IL-17 in failed outcome cases confirm the central theme that IL-17 is pathological in both human and mouse models.

The use of genetic ablation of IL-17 production specifically in neutrophils and/or IL-17R in mice would greatly enhance the rigor of this study. 

The reviewer’s point is well-taken. Having a genetic ablation of IL-17 production, specifically in the neutrophils, would be excellent. At present, however, we lack this resource. For the revised manuscript, we include the data with SR2211, a direct inhibitor of RORgt and, therefore, IL-17, in BCG-vaccinated mice.

The authors do not address the fact that numerous studies have shown that IL-17 has a protective effect in the mouse model of TB in the context of vaccination. 

Yes, there are a few articles that talk about the protective effect of IL-17 in the mouse model of TB in the context of vaccination (Khader et al. 2007; Desel et al. 2011; Choi et al. 2020). This part was discussed in the original manuscript (in the Introduction section). For the revised manuscript, we also provide results from the experiment where we blocked IL-17 production by inhibiting RORgt using SR2211 in BCG-vaccinated mice. The results clearly show IL-17 as a negative regulator of BCG-mediated protective immunity. We believe some of the reasons for the observed differences could be 1) in our study, we analysed IL-17 levels in the lung homogenates at late phases of infection, and 2) most published studies rely on ex vivo stimulation of immune cells to measure cytokine production, whereas we actually measured the cytokine levels in the lung homogenates. We will elaborate on these points in the revised version.

Finally, whether and how many times each animal experiment was repeated is unclear.

We provide the details of the number of experiments in the revised version. Briefly, the BCG vaccination experiment (Figure 1) and BCG vaccination with Celecoxib treatment experiment (Figure 6) were performed twice and thrice, respectively. The IL-17 neutralization experiment (Figure 4) and the SR2211 treatment experiment (Figure 5) were done once. We will add another SR2211 experiment data in the revised version. 

Reviewer #2 (Public review):

Summary:

In this study, Sharma et al. demonstrated that Ly6G+ granulocytes (Gra cells) serve as the primary reservoirs for intracellular Mtb in infected wild-type mice and that excessive infiltration of these cells is associated with severe bacteremia in genetically susceptible IFNγ/- mice. Notably, neutralizing IL-17 or inhibiting COX2 reversed the excessive infiltration of Ly6G+Gra cells, mitigated the associated pathology, and improved survival in these susceptible mice. Additionally, Ly6G+Gra cells were identified as a major source of IL-17 in both wild-type and IFNγ-/- mice. Inhibition of RORγt or COX2 further reduced the intracellular bacterial burden in Ly6G+Gra cells and improved lung pathology.

Of particular interest, COX2 inhibition in wild-type mice also enhanced the efficacy of the BCG vaccine by targeting the Ly6G+Gra-resident Mtb population.

Thank you for the summary.

Strengths:

The experimental results showing improved BCG-mediated protective immunity through targeting IL-17-producing Ly6G+ cells and COX2 are compelling and will likely generate significant interest in the field. Overall, this study presents important findings, suggesting that the IL-17-COX2 axis could be a critical target for designing innovative vaccination strategies for TB.

Thank you for highlighting the overall strengths of the study. 

Weaknesses:

However, I have the following concerns regarding some of the conclusions drawn from the experiments, which require additional experimental evidence to support and strengthen the overall study.

Major Concerns:

(1) Ly6G+ Granulocytes as a Source of IL-17: The authors assert that Ly6G+ granulocytes are the major source of IL17 in wild-type and IFN-γ KO mice based on colocalization studies of Ly6G and IL-17. In Figure 3D, they report approximately 500 Ly6G+ cells expressing IL-17 in the Mtb-infected WT lung. Are these low numbers sufficient to drive inflammatory pathology? Additionally, have the authors evaluated these numbers in IFN-γ KO mice? 

Thank you for pointing out the numbers in Fig. 3D It was our oversight to label the axis as No. of.  For the observation that Ly6G⁺ Gra are the major source of IL-17 in TB, we have used two separate strategies- a) IFA and b) FACS IL17<SUP>+</SUP> Ly6G<SUP>+</SUP> Gra/lung. For this data, only a part of the lung was used. For the revised manuscript, we provide the number of these cells at the whole lung level from Mtb-infected WT mice. Unfortunately, we did not evaluate these numbers in IFN-γ KO mice through FACS.. 

Our efforts to perform the IL-17 ELISpot assay on the sorted Ly6G<SUP>+</SUP>Gra from the lungs of Mtbinfected WT mice were unsuccessful. However, we provide a quantified representation of IFA of the tissue sections to stress upon the role of Ly6G<SUP>+</SUP> cells in IL-17 production in TB pathogenesis. 

(2) Role of IL-17-Producing Ly6G Granulocytes in Pathology: The authors suggest that IL-17producing Ly6G granulocytes drive pathology in WT and IFN-γ KO mice. However, the data presented only demonstrate an association between IL-17<SUP>+</SUP> Ly6G cells and disease pathology. To strengthen their conclusion, the authors should deplete neutrophils in these mice to show that IL-17 expression, and consequently the pathology, is reduced.

Thank you for this suggestion. Neutrophil depletion studies in TB remain inconclusive. In some studies, neutrophil depletion helps the pathogen (Rankin et al. 2022; Pedrosa et al. 2000; Appelberg et al. 1995), and in others, it helps the host (Lovewell et al. 2021; Mishra et al. 2017). One reason for this variability is the stage of infection when neutrophil depletion was done. However, another crucial factor is the heterogeneity in the neutrophil population. There are reports that suggest neutrophil subtypes with protective versus pathological trajectories (Nwongbouwoh Muefong et al. 2022; Lyadova 2017; Hellebrekers, Vrisekoop, and Koenderman 2018; Leliefeld et al. 2018). Depleting the entire population using anti-Ly6G could impact this heterogeneity and may impact the inferences drawn. 

A better approach would be to characterise this heterogeneous population, efforts towards which could be part of a separate study. Another direct approach could be Ly6G<SUP>+</SUP>-specific deletion of IL-17 function as part of a separate study.

For the revised manuscript, we provide results from the SR2211 experiment in BCG-vaccinated mice and other results to show the role of IL-17-producing Ly6G<SUP>+</SUP> Gra in TB pathology.   

(3) IL-17 Secretion by Mtb-Infected Neutrophils: Do Mtb-infected neutrophils secrete IL-17 into the supernatants? This would serve as confirmation of neutrophil-derived IL-17. Additionally, are Ly6G<SUP>+</SUP> cells producing IL-17 and serving as pathogenic agents exclusively in vivo? The authors should provide comments on this.

Secretion of IL-17 by Mtb-infected neutrophils in vitro has been reported earlier (Hu et al. 2017). Our efforts to do a neutrophil IL-17 ELISPOT assay were not successful, and we are still standardising it. Whether there are a few neutrophil roles exclusively seen under in vivo conditions is an interesting proposition.

(4) Characterization of IL-17-Producing Ly6G+ Granulocytes: Are the IL-17-producing Ly6G+ granulocytes a mixed population of neutrophils and eosinophils, or are they exclusively neutrophils? Sorting these cells followed by Giemsa or eosin staining could clarify this.

This is a very important point. While usually eosinophils do not express Ly6G markers in laboratory mice, under specific contexts, including infections, eosinophils can express Ly6G. Since we have not characterized these potential Ly6G<SUP>+</SUP> sub-populations, that is one of the reasons we refer to the cell types as Ly6G<SUP>+</SUP> granulocytes, which do not exclude Ly6G<SUP>+</SUP> eosinophils. A detailed characterization of these subsets could be taken up as a separate study.

Reviewer #3 (Public review):

Summary:

The authors examine how distinct cellular environments differentially control Mtb following BCG vaccination. The key findings are that IL17-producing PMNs harbor a significant Mtb load in both wild-type and IFNg^-/- mice. Targeting IL17 and Cox2 improved disease and enhanced BCG efficacy over 12 weeks and neutrophils/IL17 are associated with treatment failure in humans. The authors suggest that targeting these pathways, especially in MSMD patients may improve disease outcomes.

Thank you.

Strengths:

The experimental approach is generally sound and consists of low-dose aerosol infections with distinct readouts including cell sorting followed by CFU, histopathology, and RNA sequencing analysis. By combining genetic approaches and chemical/antibody treatments, the authors can probe these pathways effectively.

Understanding how distinct inflammatory pathways contribute to control or worsen Mtb disease is important and thus, the results will be of great interest to the Mtb field

Thank you.

Weaknesses:

A major limitation of the current study is overlooking the role of non-hematopoietic cells in the IFNg/IL17/neutrophil response. Chimera studies from Ernst and colleagues (Desvignes and Ernst 2009) previously described this IDO-dependent pathway following the loss of IFNg through an increased IL17 response. This study is not cited nor discussed even though it may alter the interpretation of several experiments.

Thank you for pointing out this earlier study, which we concede, we missed discussing. We disagree on the point that results from that study may alter the interpretation of several experiments in our study. On the contrary, the main observation that loss of IFNγ causes severe IL-17 levels is aligned in both studies.

IDO1 is known to alter T-helper cell differentiation towards Tregs and away from Th17 (Baban et al. 2009). It is absolutely feasible for the non-hematopoietic cells to regulate these events. However, that does not rule out the neutrophil production of IL-17 and the downstream pathological effect shown in this study. We have discussed and cited this study in the revised manuscript.

Several of the key findings in mice have previously been shown (albeit with less sophisticated experimentation) and human disease and neutrophils are well described - thus the real new finding is how intracellular Mtb in neutrophils are more refractory to BCG-mediated control. However, given there are already high levels of Mtb in PMNs compared to other cell types, and there is a decrease in intracellular Mtb in PMNs following BCG immunization the strength of this finding is a bit limited.

The reviewer’s interpretation of the BCG-refractory Mtb population in the neutrophil is interesting. The reviewer is right that neutrophils had a higher intracellular Mtb burden, which decreased in the BCG-vaccinated animals. Thus, on that account, the reviewer rightly mentions that BCG is able to control Mtb even in neutrophils. However, BCG almost clears intracellular burden from other cell types analysed, and therefore, the remnant pool of intracellular Mtb in the lungs of BCG-vaccinated animals could be mostly those present in the neutrophils. This is a substantial novel development in the field and attracts focus towards innate immune cells for vaccine efficacy. 

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Reviewer #1 (Recommendations for the authors):

All figures: Clear information about the number of repeat experiments for each figure must be included.

We have provided the details of the number of repeat experiments in the revised version.

Figure 1: The claim that neutrophils are a dominant cell type infected during Mtb infection of the lungs is undermined by the limited number of markers used to identify cell types. The gating strategy used to initially identify what cells are infected with Mtb divided cells into three categories; granulocytes (Ly6G<SUP>+</SUP> Cd11b<SUP>+</SUP>), CD64+MerTK+ macrophages, or Sca1+CD90.1+CD73+ (mesenchymal stem cells). This strategy leaves out monocyte populations that have been shown to be the dominant infected cells in other strategies (most recently, PMID: 36711606).

Thank you for this important point. We agree that we did not assess the infected monocyte population, specifically the Cd11c<SUP>+</SUP> population. Both CD11c<SUP>Hi</SUP> and CD11c<SUP>Lo</SUP> monocyte cells appear to be important for Mtb infection, in different studies (Lee et al., 2020), (Zheng et al., 2024). Therefore, leaving out the CD11c<SUP>+</SUP> population in our assays was a conscious decision to ensure the clarity of the cell types being studied. 

In addition, substantial evidence from multiple studies indicates that Ly6G⁺ granulocytes constitute the predominant infected population in the Mtb-infected lungs of both mice and humans (Lovewell et al., 2021) (Eum et al., 2010). While monocytes may contribute to Mtb infection dynamics, our findings align with a growing body of research emphasizing the significant role of neutrophils as a dominant infected cell type in the lungs during TB pathology.  

Figure 1: Putting the data from separate panels together, it appears that very few bacteria are isolated from the three cell types in the lung, suggesting there may be some loss in the preparation steps. Why is the total sorted CFU from neutrophils, macrophages, and MSCs so low, <400 bacteria total, when the absolute CFU is so high? Is it because only a fraction of the lung is being sorted/plated?

Yes, only a fraction of the lung was used for cell sorting and subsequent plating. The CFU plating from sorted cells also does not account for any bacteria growing extracellularly.

Figure 3C: It is difficult to ascertain whether the gating on IL-17<SUP>+</SUP> cells is accurately identifying IL-17 producing cells. It is surprising, based on other published work, that the authors claim that almost half of CD45+CD11b-Ly6G- cells produce IL-17 in WT mice. It would be informative to show cell type-specific production of IL-17 in both WT and IFN-γ KO mice for comparison with the literature. Unstained/isotype controls for IL-17 staining should be shown. With this in mind, it is difficult to interpret the authors' claim that 80% of neutrophils produce IL-17.

Thank you for the points above. We do agree that we were surprised to see ~50% of CD45<SUP>+</SUP> CD11b<SUP>-</SUP>Ly6G<SUP>-</SUP> cells producing IL-17. We have now done multiple experiments to confirm that this number is actually less than 1% (~90 cells) in the uninfected mice and less than 4% (~4000) in the Mtb-infected mice.

Neutrophil-derived IL-17 production in Mtb-infected lungs is supported by two independent techniques in our current study: Flow Cytometry and Immunofluorescence assay. While  Neutrophil production of IL-17 is rarely studied in the context of TB, in several other settings it has been widely reported (Gonzalez-Orozco et al., 2019; Li et al., 2010; Ramirez-Velazquez et al., 2013). We consistently get >60% IL-17 positive cells in the CD11b<SUP>+</SUP> Ly6G<SUP>+</SUP> population, specifically in the infected samples. 

To specifically address the reviewer’s concerns, we have now used an isotype control for IL17 staining and show the specificity of IL-17A antibody binding. The Author response image 1 is from the uninfected mice, 8 weeks age.

Unfortunately, our efforts to establish an IL-17  ELISPOT assay from neutrophils were not very successful and need further standardisation. The new results are included in Fig. 3C-D and Fig. S2F-G in the revised manuscript.

Author response image 1.

Figure 3 D-H. Quantification of immunofluorescence microscopy should be provided.

In the revised manuscript, we provide the quantification of IFA results.

Figure 4: Effects on neutrophil numbers in IFN-γ Kos do not correlate with CFU reductions, suggesting there may be a neutrophilindependent mechanism.

In the IFN-γ KO, we agree that the effect was less than dramatic. The immune dysfunction in the IFN-γ KO mice is too severe to see a strong reversal in the phenotype through interventions. 

While we do not rule out any neutrophil-independent mechanism, in the context of following observations, neutrophil-dependent mechanisms certainly appear to play an important role-

(a) Improved pathology and survival upon IL-17 neutralization, which further improves with the inclusion of celecoxib.

(b) Loss of IL17⁺-Ly6G⁺ cells upon IL-17 neutralization, which is further exacerbated when combined with celecoxib.

(c) Significant reduction in PMN number (shown by FACS) without any major impact on Th17 cell population upon IL-17 neutralization.

Finally, we believe some of the observations may become stronger once we characterize the specific sub-population among the Ly6G+ cells that correlates with pathology. For example, as shown in Figure 4I, FACS analysis of the Ly6G^⁺ cell population in Mtb-infected IFNγ^⁻/⁻ mice revealed a substantial subset of CD11b^mid Ly6G^ʰⁱ cells, indicative of an immature neutrophil population (Scapini et al., 2016). Efforts are currently underway to identify these important subpopulations.  

Figure 4: Differences observed in the spleen cannot be connected to dissemination per se but instead could be a result of enhanced immune control in the spleen.

Thank you for this important point. We have revised this section. The role of neutrophils in Mtb dissemination is an emerging area of research, with growing evidence suggesting that these cells contribute to the spread of Mtb beyond the lungs (Hult et al., 2021). We highlight that the observed correlation could be speculative at this juncture.

Figure 4, 5: IL-17 neutralization alone has no effect on CFU in the lungs of Mtb-infected mice. While the combination of IL-17 neutralization and celecoxib has a very modest effect on CFU, the mechanism behind this observation is unclear. Further, the experiment shown has only 3 mice per group and it is unclear whether this (or any other) mouse experiment was repeated.

For Fig. 4, the experiment was done with 3 mice/group. The IFN KO mice were used to help identify the mechanism. IL-17 neutralisation or Celecoxib treatment alone did not have any significant effect on the bacterial burden (in lungs or isolated PMNs). However, it did show a significant effect on the number of PMNs recruited. Combination of IL-17 neutralisation and celecoxib led to about a one-log decrease in CFU, which is significant.

For Fig. 5, we used SR2211 instead of anti-IL-17 Ab for the experiment. This experiment had WT mice and 5 animals/group. Here, celecoxib and SR2211 alone showed a significant decline in PMN-resident Mtb pool as well as spleen burden. Only in the lungs, the impact of SR2211 alone was not significant.

Figure 6: The decreases in CFU correlate with a decrease in neutrophils; nothing connects this to neutrophil production of IL-17.

We now show quantification of observation in Fig. 5I, where in the WT mice, treatment with Celecoxib reduces the frequency of IL-17-producing Ly6G+ cells. In the revised manuscript, we also show direct evidence of SR2211 activity on BCG vaccine efficacy, which causes a significant decline in the Mtb burden in whole lung or in the isolated PMNs.

Figure 7. The Human data shows that elevated neutrophil levels and elevated IL-17 levels are associated with treatment failure in TB patients. This is expected, and does not

The literature lacks consensus in terms of a protective or pathological role of IL-17 in TB. Therefore, it was not expected to see higher IL-17 in patients who experienced relapse, death, or failed treatment outcomes. We do not have evidence from human subjects whether neutrophil derived IL-17 has a similar pathological role as observed in mice. However, higher IL-17 in failed outcome cases confirm the central theme that IL-17 is pathological in both human and mouse models.

Reviewer #2 (Recommendations for the authors):

(1) Survival of IFN-γ-/- Mice: The survival of IFN-γ-/- mice up to 100 days following a challenge with ~100 CFU of H37Rv is quite unusual. Have the authors checked PDIM expression in their Mtb strain, given that several studies report earlier mortality in these mice?

As shown in Fig. 4F, H37Rv-infected IFN-γ⁻/⁻ mice survived up to a little over 80 days. These figures are not unusual in the light of the following:

(1) In one study, IFNγ⁻/⁻ survived for about 40 days when the hypervirulent Mtb strain was used to infect these mice at 100-200 CFU using nose-only aerosol exposure (Nandi and Behar, 2011)

(2) In yet another study, IFNγ⁻/⁻ mice survived for ~50 days, however, they used H37Rv at 1-3x10⁵ CFU to infect through intravenous injection (Kawakami et al., 2004)

Thus, compared with the above observations, where IFN-γ^-/- mice survived for maximum 50 days due to hypervirulent infection or a very high dose infection, infection with H37Rv at ~100 CFU through the aerosol route and surviving for ~80 days is not unusual. The H37Rv cultures used in our study are always animal-passaged to ensure PDIM integrity.

(2) Granuloma Scoring: The granuloma scores appear to represent the percentage of lesion area. Please clarify and, if necessary, amend this in the manuscript.

The granuloma score is based on the calculation of the number of granulomatous infiltration and their severity. These are not % lesion area. We have added this detail in the revised manuscript.

(3) Pathology Comparison in Figures 4F and 4G: Does the pathology shown in Figure 4G correspond to the same groups as in Figure 4F? The celecoxib group in Figure 4F and the WT group in Figure 4G seem to be missing. Please clarify.

Figures 4F and 4G depict two independent experiments. For the time-to-death experiment, we had to leave the animals. The rest of the panels in Fig. 4 represent animals from the same experiment.

(4) Effect of Celecoxib on Ly6G+ Cells: The authors demonstrated that celecoxib treatment reduces Ly6G+ cells and IL-17-producing Ly6G+ cells. Do Ly6G+ cells express EP2/EP4 receptors? Alternatively, could the reduction in IL-17-producing Ly6G+ cells be due to an improved bactericidal response in other innate cells? The authors should discuss this possibility.

Yes, Ly6G^⁺ granulocytes express EP2/EP4 receptors (Lavoie et al., 2024), which mediate PGE₂ signaling. Prostaglandin E_₂ (PGE_₂) is known to regulate neutrophil function and can enhance IL-17 production in various immune cells (Napolitani et al., 2009). However, the expression and functional role of EP2/EP4 receptors specifically on Ly6G^⁺ granulocytes in the context of Mtb infection require further investigation.

The alternate suggestion by the reviewer that the reduction in IL-17-producing Ly6G^⁺ cells following celecoxib treatment could be attributed to an improved bactericidal response in other innate immune cells is attractive. While we did not experimentally rule out this possibility, since reduced IL-17 invariably associated with reduced neutrophil-resident Mtb population, a cell-autonomous mechanism operational in Ly6G+ granulocytes is a highly likely mechanism.  

(5) Culture Conditions: The methods section indicates that bacteria were cultured in 7H9+ADC. Is there a specific reason why the Oleic acid supplement was not added, given that standard Mtb culture conditions typically use 7H9+OADC supplements? Please comment on this choice.

It is a standard microbiological experimental procedure to use 7H9+ADC for broth culture, while 7H11+OADC for solid culture. Compared to broth culture, solid media are usually more stressful for bacteria because of hypoxia inside the growing colonies. Therefore, the media used are enriched in casein hydrolysate (like 7H11) and oleic acid (OADC).

Reviewer #3 (Recommendations for the authors):

Major suggestion: To really determine the role of neutrophil IL17 will require depletion studies and chimera experiments. These are clearly a major undertaking. I believe making significant re-writes to alter the conclusions or reanalyze any data to determine the role of nonhematopoietic and hematopoietic cells in IL17 is needed. If the conclusions are left as is, further experimentation is needed to fully support those conclusions.

Thank you for the suggestion. We have embarked on the specific deletion studies; however, as mentioned, this is a major undertaking and will take time. As suggested, we have discussed the results in accordance with the strength of evidence currently provided.

Eum, S.Y., J.H. Kong, M.S. Hong, Y.J. Lee, J.H. Kim, S.H. Hwang, S.N. Cho, L.E. Via, and C.E. Barry, 3rd. 2010. Neutrophils are the predominant infected phagocyGc cells in the airways of paGents with acGve pulmonary TB. Chest 137:122-128.

Gonzalez-Orozco, M., R.E. Barbosa-Cobos, P. Santana-Sanchez, L. Becerril-Mendoza, L. Limon-

Camacho, A.I. Juarez-Estrada, G.E. Lugo-Zamudio, J. Moreno-Rodriguez, and V. OrGzNavarrete. 2019. Endogenous sGmulaGon is responsible for the high frequency of IL-17Aproducing neutrophils in paGents with rheumatoid arthriGs. Allergy Asthma Clin Immunol 15:44.

References

Hult, C., J.T. Ma[la, H.P. Gideon, J.J. Linderman, and D.E. Kirschner. 2021. Neutrophil Dynamics Affect Mycobacterium tuberculosis Granuloma Outcomes and DisseminaGon. Front Immunol 12:712457.

Kawakami, K., Y. Kinjo, K. Uezu, K. Miyagi, T. Kinjo, S. Yara, Y. Koguchi, A. Miyazato, K. Shibuya, Y. Iwakura, K. Takeda, S. Akira, and A. Saito. 2004. Interferon-gamma producGon and host protecGve response against Mycobacterium tuberculosis in mice lacking both IL-12p40 and IL-18. Microbes Infect 6:339-349.

Lavoie, J.C., M. Simard, H. Kalkan, V. Rakotoarivelo, S. Huot, V. Di Marzo, A. Cote, M. Pouliot, and N. Flamand. 2024. Pharmacological evidence that the inhibitory effects of prostaglandin E2 are mediated by the EP2 and EP4 receptors in human neutrophils. J Leukoc Biol 115:1183-1189.

Lee, J., S. Boyce, J. Powers, C. Baer, C.M. Sasse[, and S.M. Behar. 2020. CD11cHi monocyte-derived macrophages are a major cellular compartment infected by Mycobacterium tuberculosis. PLoS Pathog 16:e1008621.

Li, L., L. Huang, A.L. Vergis, H. Ye, A. Bajwa, V. Narayan, R.M. Strieter, D.L. Rosin, and M.D. Okusa. 2010. IL-17 produced by neutrophils regulates IFN-gamma-mediated neutrophil migraGon in mouse kidney ischemia-reperfusion injury. J Clin Invest 120:331-342.

Lovewell, R.R., C.E. Baer, B.B. Mishra, C.M. Smith, and C.M. Sasse[. 2021. Granulocytes act as a niche for Mycobacterium tuberculosis growth. Mucosal Immunol 14:229-241.

Nandi, B., and S.M. Behar. 2011. RegulaGon of neutrophils by interferon-gamma limits lung inflammaGon during tuberculosis infecGon. The Journal of experimental medicine 208:22512262.

Napolitani, G., E.V. Acosta-Rodriguez, A. Lanzavecchia, and F. Sallusto. 2009. Prostaglandin E2 enhances Th17 responses via modulaGon of IL-17 and IFN-gamma producGon by memory CD4+ T cells. Eur J Immunol 39:1301-1312.

Ramirez-Velazquez, C., E.C. CasGllo, L. Guido-Bayardo, and V. OrGz-Navarrete. 2013. IL-17-producing peripheral blood CD177+ neutrophils increase in allergic asthmaGc subjects. Allergy Asthma Clin Immunol 9:23.

Sadikot, R.T., H. Zeng, A.C. Azim, M. Joo, S.K. Dey, R.M. Breyer, R.S. Peebles, T.S. Blackwell, and J.W. Christman. 2007. Bacterial clearance of Pseudomonas aeruginosa is enhanced by the inhibiGon of COX-2. Eur J Immunol 37:1001-1009.

Zheng, W., I.C. Chang, J. Limberis, J.M. Budzik, B.S. Zha, Z. Howard, L. Chen, and J.D. Ernst. 2023. Mycobacterium tuberculosis resides in lysosome-poor monocyte-derived lung cells during chronic infecGon. bioRxiv 

Zheng, W., I.C. Chang, J. Limberis, J.M. Budzik, B.S. Zha, Z. Howard, L. Chen, and J.D. Ernst. 2024. Mycobacterium tuberculosis resides in lysosome-poor monocyte-derived lung cells during chronic infecGon. PLoS Pathog 20:e1012205.

Author response:

Reviewer #1 (Public review):

Summary:

The manuscript by Yang et al. investigates the relationship between multi-unit activity in the locus coeruleus, putatively noradrenergic locus coeruleus, hippocampus (HP), sharp-wave ripples (SWR), and spindles using multi-site electrophysiology in freely behaving male rats. The study focuses on SWR during quiet wake and non-REM sleep, and their relation to cortical states (identified using EEG recordings in frontal areas) and LC units.

The manuscript highlights differential modulation of LC units as a function of HP-cortical communication during wake and sleep. They establish that ripples and LC units are inversely correlated to levels of arousal: wake, i.e., higher arousal correlates with higher LC unit activity and lower ripple rates. The authors show that LC neuron activity is strongly inhibited just before SWR is detected during wake. During non-REM sleep, they distinguish "isolated" ripples from SWR coupled to spindles and show that inhibition of LC neuron activity is absent before spindle-coupled ripples but not before isolated ripples, suggesting a mechanism where noradrenaline (NA) tone is modulated by HP-cortical coupling. This result has interesting implications for the roles of noradrenaline in the modulation of sleep-dependent memory consolidation, as ripple-spindle coupling is a mechanism favoring consolidation. The authors further show that NA neuronal activity is downregulated before spindles.

Strengths:

In continuity with previous work from the laboratory, this work expands our understanding of the activity of neuromodulatory systems in relation to vigilance states and brain oscillations, an area of research that is timely and impactful. The manuscript presents strong results suggesting that NA tone varies differentially depending on the coupling of HP SWR with cortical spindles. The authors place their findings back in the context of identified roles of HP ripples and coupling to cortical oscillations for memory formation in a very interesting discussion. The distinction of LC neuron activity between awake, ripple-spindle coupled events and isolated ripples is an exciting result, and its relation to arousal and memory opens fascinating lines of research.

Weaknesses:

I regretted that the paper fell short of trying to push this line of idea a bit further, for example, by contrasting in the same rats the LC unit-HP ripple coupling during exploration of a highly familiar context (as seemingly was the case in their study) versus a novel context, which would increase arousal and trigger memory-related mechanisms. Any kind of manipulation of arousal levels and investigation of the impact on awake vs non-REM sleep LC-HP ripple coordination would considerably strengthen the scope of the study.

We agree that conducting specific behavioral tests before electrophysiological recordings, as well as manipulating arousal during the recording session, would strengthen the study. These experiments are planned for future work, and we will acknowledge this point in the discussion.

The main result shows that LC units are not modulated during non-REM sleep around spindle-coupled ripples (named spRipples, 17.2% of detected ripples); they also show that LC units are modulated around ripple-coupled spindles (ripSpindles, proportion of detected spindles not specified, please add). These results seem in contradiction; this point should be addressed by the authors.

We found that LC suppression was generally weak around both types of coupled events (spRipples and ripSpindles). Specifically, session-averaged spRipple-associated LC suppression reached a significance level (exceeding 95% CI) in 4 (n = 3 rats) out of 20 sessions (Line 177). The significant ripSpindle-associated LC suppression was observed in 3 (n = 2 animals) out of 20 sessions (Line 213). When comparing the modulation index (MI) around spRipples and ripSpindles, we found a significant correlation (Pearson r = 0.72, p = 0.0003). As shown in Author response image 1 below, the three sessions (blue square, MI < 95%CI) with significant ripSpindle-associated LC suppression coincide with those sessions showing LC modulation around spRipples. Although, the detection of coupled events was performed independently, some overlap can not be excluded. We will be happy to provide this additional information in the results section.

Author response image 1.

Results are displayed per recording session, with 20 sessions total recorded from 7 rats (2 to 8 sessions per rat), which implies that one of the rats accounts for 40% of the dataset. Authors should provide controls and/or data displayed as average per rat to ensure that results are now skewed by the weight of that single rat in the results.

Since high-quality recordings from the LC in behaving rats are challenging and rare, we used all valid sessions for this study. In Author response image 2 below, we plotted the average MIs for each animal (A) and each session (B). The dashed lines indicate the mean ± 2 standard deviations across all sessions. The rat ID and number of sessions is indicated in parentheses in A. All animal-averaged MIs fall within this range, indicating that the MI distribution is not driven by a single animal (rat 1101, 8 sessions). The MIs of eight sessions from rat1101 are shown in grey-filled triangles (B). Comparison of the MI distribution for these eight sessions versus the remaining 12 sessions from six other animals revealed no significant difference (Kolmogorov-Smirnov test, p = 0.969). We will be happy to provide this additional information in the Results section.

Author response image 2.

In its current form, the manuscript presents a lack of methodological detail that needs to be addressed, as it clouds the understanding of the analysis and conclusions. For example, the method to account for the influence of cortical state on LC MUA is unclear, both for the exact methods (shuffling of the ripple or spindle onset times) and how this minimizes the influence of cortical states; this should be better described. If the authors wish to analyze unit modulation as a function of cortical state, could they also identify/sort based on cortical states and then look at unit modulation around ripple onset? For the first part of the paper, was an analysis performed on quiet wake, non-REM sleep, or both?

As shown in Figure 3A and described in the main text (Lines 113–116), LC firing rate was negatively correlated with cortical arousal as quantified by Synchronisation Index (SI), whereas ripple rate was positively correlated with arousal. When computing LC activity (0.05 sec bins) aligned to the ripple onset over a longer time window ([–12, 12] sec), we observed a slow decrease in the LC firing rate beginning as early as 10 s before the ripple onset. In Author response image 3 below, a blue trace shows this slower temporal dynamic in a representative session. In addition to LC activity modulation at this relatively slow temporal scale, we also observed a much sharper drop in the LC firing rate ~ 2 s before the ripple onset. Considering two temporal scales, we hypothesized that slow modulation of LC activity might be related to fluctuations of the global brain state. Specifically, a higher SI (more synchronized cortical population activity) corresponded to a lower arousal state and reduced LC tonic firing; this brain state was associated with a higher ripple activity. Thus, slow LC modulation was likely driven by cortical state transitions. To correct for the influence of the global brain state on the LC/ripple temporal dynamics, we generated surrogate events by jittering the times of detected ripples (Lines 415–421). First, we confirmed that the cortical state did not differ around ripples and surrogate events (Figure 3C), while triggering the hippocampal LFP on the surrogate events lacked the ripple-specific frequency component (Figure 3B,). Thus, LC activity around surrogate evens captured its cortical state dependent dynamics (see orange trace in Author response image 3 below). Finally, to characterize state-independent ripple-related LC activity, we subtracted the state-related LC activity (orange trace in Author response image 3 below) from the ripple-triggered LC activity (blue trace). This yielded a corrected estimate of ripple-associated LC activity that was largely free from the confounding influence of cortical state transitions.

Author response image 3.

In the results subsection “LC-NE neuron spiking is suppressed around hippocampal ripples”, we reported LC modulation without accounting for the cortical state. The state-dependent effects were instead examined in the subsequent subsection, “Peri-ripple LC modulation depends on the cortical–hippocampal interaction,” where we characterized LC activity around ripples across different cortical states (quite awake and NREM sleep). We will provide more methodological details and a rationale for each analysis, as requested.

Reviewer #2 (Public review):

Summary:

In this study, the authors studied the synchrony between ripple events in the Hippocampus, cortical spindles, and Locus Coeruleus spiking. The results in this study, together with the established literature on the relationship of hippocampal ripples with widespread thalamic and cortical waves, guided the authors to propose a role for Locus Coeruleus spiking patterns in memory consolidation. The findings provided here, i.e., correlations between LC spiking activity and Hippocampal ripples, could provide a basis for future studies probing the directional flow or the necessity of these correlations in the memory consolidation process. Hence, the paper provides enough scientific advances to highlight the elusive yet important role of Norepinephrine circuitry in the memory processes.

Strengths:

The authors were able to demonstrate correlations of Locus Coeruleus spikes with hippocampal ripples as well as with cortical spindles. A specific strength of the paper is in the demonstration that the spindles that activate with the ripples are comparatively different in their correlations with Locus Coeruleus than those that do not.

Weaknesses:

The claims regarding the roles of these specific interactions were mostly derived from the literature that these processes individually contribute to the memory process, without any evidence of these specific interactions being necessary for memory processes. There are also issues with the description of methods, validation of shuffling procedures, and unclear presentation and the interpretation of the findings, which are described in the points that follow. I believe addressing these weaknesses might improve and add to the strength of the findings.

We believe that our responses to the Reviewer 1 and planned revisions as described above will adequately address the issues raised by the Reviewer 2. 

Reviewer #3 (Public review):

Summary:

This manuscript examines how locus coeruleus (LC) activity relates to hippocampal ripple events across behavioral states in freely moving rats. Using multi-site electrophysiological recordings, the authors report that LC activity is suppressed prior to ripple events, with the magnitude of suppression depending on the ripple subtype. Suppression is stronger during wakefulness than during NREM sleep and is least pronounced for ripples coupled to spindles.

Strengths:

The study is technically competent and addresses an important question regarding how LC activity interacts with hippocampal and thalamocortical network events across vigilance states.

Weaknesses:

The results are interesting, but entirely observational. Also, the study in its current form would benefit from optimization of figure labeling and presentation, and more detailed result descriptions to make the findings fully interpretable. Also, it would be beneficial if the authors could formulate the narrative and central hypothesis more clearly to ease the line of reasoning across sections.

We will do our best to optimize presentation, revise the main text and figure labelling. When appropriate, we will add specific hypotheses and a rationale for specific analyses.

Comments:

(1) Stronger evidence that recorded units represent noradrenergic LC neurons would reinforce the conclusions. While direct validation may not be possible, showing absolute firing rates (Hz) across quiet wake, active wake, NREM, and REM, and comparing them to published LC values, would help.

We will provide the requested data in the revised manuscript.

(2) The analyses rely almost exclusively on z-scored LC firing and short baselines (~4-6 s), which limits biological interpretation. The authors should include absolute firing rates alongside normalized values for peri-ripple and peri-spindle analyses and extend pre-event windows to at least 20-30 s to assess tonic firing evolution. This would clarify whether differences across ripple subtypes arise from ceiling or floor effects in LC activity; if ripples require LC silence, the relative drop will appear larger during high-firing wake states. This limitation should be discussed and, if possible, results should be shown based on unnormalized firing rates.

We can provide absolute firing rates alongside normalized values for peri-ripple and peri-spindle analyses for isolated single LC units. However, we are reluctant to average absolute firing rates for multiunit activity, as it is unknown how many neurons contributed to each MUA recording. We can add the plots with extended pre-event windows ([–12, 12] sec). Please see our response to the Reviewer 1 about the two temporal scales of LC modulation.

(3) Because spindles often occur in clusters, the timing of ripple occurrence within these clusters could influence LC suppression. Indicate whether this structure was considered or discuss how it might affect interpretation (e.g., first vs. subsequent ripples within a spindle cluster).

We did not consider spindle clusters and classified the event as ripple coupled spindle if the ripple occurred between the spindle on- and offset. We will clarify this point in the Method section. 

(4) While the observational approach is appropriate here, causal tests (e.g., optogenetic or chemogenetic manipulation of LC around ripple events and in memory tasks) would considerably strengthen the mechanistic conclusions. At a minimum, a discussion of how such approaches could address current open questions would improve the manuscript.

We agree that conducting causal tests would strengthen the study. We will acknowledge in the discussion that our results shall inspire future studies addressing many open questions.

(5) Please show how "Synchronization Index" (SI) differs quantitatively across behavioral states (wake, NREM, REM) and discuss whether it could serve as a state classifier. This would strengthen interpretations of the correlations between SI, ripple occurrence, and LC activity.

We will add the plot showing the average SI values across behavioral states. Although SI could potentially serve as a classifier, we have chosen not to discuss this in detail to maintain focus in the discussion.

(6) The current use of SI to denote a delta/gamma power ratio is unconventional, as "SI" typically refers to phase-locking metrics. Consider adopting a more standard term, such as delta/gamma power ratio. Similarly, it would be easier to follow if you use common terminology (AUC) to describe the drop in LC-MUA rather than using "MI" and "sub-MI".

The ranges of delta and gamma bands might vary across studies; therefore, we prefer using SI, as defined here and in our previous publications (Yang, 2019; Novitskaya, 2012). We calculated the modulation index (MI) as the area under the curve of the peri-event time histogram within the 1 second preceding ripple onset. To avoid potential confusion with the AUC calculated over the entire signal window, we opted to use MI. 

(7) The logic in Figure 3 is difficult to follow. The brain state (delta/gamma ratio) appears unchanged relative to surrogate events (3C), while LC activity that is supposedly negatively correlated to delta/gamma changes markedly (3D-E). Could this discrepancy reflect the low temporal resolution (4-s windows) used to calculate delta/gamma when the changes occur on a shorter time scale?

Figure 3D and 3E show the 'state-corrected' ripple-related LC activity. Specifically, the cortical state related LC modulation was subtracted from the non-corrected ripple-associated LC activity. Please, see our detailed response to the Reviewer 1. We will revise the results and Figure 3 legend to clarify this point.

(8) There are apparent inconsistencies between Figures 4B and 4C-D. In B, it seems that the difference between the 10th and 90th percentile is mostly in higher frequencies, but in C and D, the only significant difference is in the delta band.

We will re-do this analysis and clarify this inconsistency.

(9) Because standard sleep scoring is based on EEG and EMG signals, please include an example of sleep scoring alongside the data used for state classification. It would also be relevant to include the delta/gamma power ratio in such an example plot.

We removed ‘standard’ and will add a supplementary Figure illustrating sleep scoring.

(10) Can variability in modulation index (subMI) across ripple subsets reflect differences in recording quality? Please report and compare mean LC firing rates across subsets to confirm this is not a confounding factor.

We will plot this result averaged per rat.

(11) Figure 6B: If the brown trace represents LC-MUA activity around random time points, why would there be a coinciding negative peak as relative to real sleep spindles? Or is it the subtracted trace?

We will clarify this point in the figure legend.

(12) On page 8, lines 207-209, the authors write "Importantly, neither the LC-MUA rate nor SIs differed during a 2-sec time window preceding either group of spindles". It is unclear which data they refer to, but the statement seems to contradict Figure 6E as well as the following sentence: "Across sessions, MI values exceeded 95% CI in 17/20 datasets for isoSpindles and only 3/20 for ripSpindles". This should be clarified.

We will clarify the description of this result.

(13) The results in Figures 5C and 6F do not align. It seems surprising that ripple-coupled spindles show a considerably higher LC modulation than spindle-coupled ripples, as these events should overlap. Could the discrepancy be due to Z-score normalization as mentioned above? Please include a discussion of this to help the interpretation of the results.

We will clarify this point in the revised manuscript. Please, also see our response to the Reviewer 1.

(14) The text implies that 8 recordings came from one rat and two each from six others. This should be confirmed, and it should be explained how the recordings were balanced and analyzed across animals.

Since high-quality recordings from LC in behaving animals are challenging and rare, we used all valid sessions. We will also present the main results averaged per rat, as also requested by the Reviewer 1.

Author response:

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

Reviewer #1 (Public review):

Summary:

Syed et al. investigate the circuit underpinnings for leg grooming in the fruit fly. They identify two populations of local interneurons in the right front leg neuromere of ventral nerve cord, i.e. 62 13A neurons and 64 13B neurons. Hierarchical clustering analysis identifies 10 morphological classes for both populations. Connectome analysis reveals their circuit interactions: these GABAergic interneurons provide synaptic inhibition either between the two subpopulations, i.e., 13B onto 13A, or among each other, i.e., 13As onto other 13As, and/or onto leg motoneurons, i.e., 13As and 13Bs onto leg motoneurons. Interestingly, 13A interneurons fall into two categories, with one providing inhibition onto a broad group of motoneurons, being called "generalists", while others project to a few motoneurons only, being called "specialists". Optogenetic activation and silencing of both subsets strongly affect leg grooming. As well aas ctivating or silencing subpopulations, i.e., 3 to 6 elements of the 13A and 13B groups, has marked effects on leg grooming, including frequency and joint positions, and even interrupting leg grooming. The authors present a computational model with the four circuit motifs found, i.e., feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. This model can reproduce relevant aspects of the grooming behavior.

Strengths:

The authors succeeded in providing evidence for neural circuits interacting by means of synaptic inhibition to play an important role in the generation of a fast rhythmic insect motor behavior, i.e., grooming. Two populations of local interneurons in the fruit fly VNC comprise four inhibitory circuit motifs of neural action and interaction: feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. Connectome analysis identifies the similarities and differences between individual members of the two interneuron populations. Modulating the activity of small subsets of these interneuron populations markedly affects the generation of the motor behavior, thereby exemplifying their important role in generating grooming.

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

Weaknesses:

Effects of modulating activity in the interneuron populations by means of optogenetics were conducted in the so-called closed-loop condition. This does not allow for differentiation between direct and secondary effects of the experimental modification in neural activity, as feedforward and feedback effects cannot be disentangled. To do so, open loop experiments, e.g., in deafferented conditions, would be important. Given that many members of the two populations of interneurons do not show one, but two or more circuit motifs, it remains to be disentangled which role the individual circuit motif plays in the generation of the motor behavior in intact animals.

Our optogenetic experiments show a role for 13A/B neurons in grooming leg movements – in an intact sensorimotor system - but we cannot yet differentiate between central and reafferent contributions. Activation of 13As or 13Bs disinhibits motor neurons and that is sufficient to induce walking/grooming. Therefore, we can show a role for the disinhibition motif.

Proprioceptive feedback from leg movements could certainly affect the function of these reciprocal inhibition circuits. Given the synapses we observe between leg proprioceptors and 13A neurons, we think this is likely.