eLife assessment

Working with a diverse panel of field-grown rice accessions, this valuable study measures changes in transcript abundance, tests for patterns of selection on gene expression, and maps the genetic basis of variation in gene expression in normal and high salinity conditions. The authors provide solid evidence that salinity treatment increases the number of genes with mean expression levels away from the optimum, and that a relatively small number of genes are hotspots for genetic variants that affect genome-wide patterns of variation in gene expression under high salinity. The design, clarity, and interpretation of several statistical analyses can be improved, additional opportunities for integration among datasets and analyses could be realized, and genetic manipulation would be required to confirm the functional involvement of any specific genes in regulatory networks or organismal traits that confer adaptation to higher salinity conditions. The manuscript will not only be of interest to evolutionary biologists studying the genetics of complex traits, but it will also be a resource for plant biologists studying mechanisms of abiotic stress tolerance.

Reviewer #1 (Public Review):

Summary:

Understanding the mechanisms of how organisms respond to environmental stresses is a key goal of biological research. Assessment of transcriptional responses to stress can provide some insights into those underlying mechanisms. The researchers quantified traits, fitness, and gene expression (transcriptional) response to salinity stress (control vs stress treatments) for 130 accessions of rice (three replicates for each accession), which were grown in the field in the Philippines. This experimental design allowed for many different types of downstream analyses to better understand the biology of the system. These analyses included estimating the strength of selection imposed on transcription in each environment, evaluating possible trade-offs in gene expression, testing whether salinity induces transcriptional decoherence, and conducting various eQTL-type analyses.

Strengths:

The study provides an extensive analysis of gene expression responses to stress in rice and offers some insights into underlying mechanisms of salinity responses in this important crop system. The fact that the study was conducted under field conditions is a major plus, as the gene expression responses to soil salinity are more realistic than if the study was conducted in a greenhouse or growth chamber. The preprint is generally well-written and the methods and results are mostly well-described.

Weaknesses:

While the study makes good use of analyzing the dataset, it is not clear how the current work advances our understanding of gene regulatory evolution or plant responses to soil salinity generally. Overall, the results are consistent with other prior studies of gene expression and studies of selection across environmental conditions. Some of the framing of the paper suggests that there is more novelty to this study than there is in reality. That said, the results will certainly be useful for those working in rice and should be interesting to scientists interested in how gene expression responses to stress occur under field conditions. I detail other concerns I had about the preprint below:

The abstract on lines 33-35 illustrates some of my concerns about the overstatement of the novelty of the current study. For example, is it really true that the role of gene expression in mediating stress response and adaptation is largely unexplored? There have been numerous studies that have evaluated gene expression responses to stresses in a wide range of organisms. Perhaps, I am missing something critically different about this study. If so, I would recommend that the authors reword this sentence to clarify what gap is being filled by this study. Further, is it really the case that none of them have evaluated how the correlational structure of gene expression changes in response to stresses in plants, as implied in lines 263-265? Don't the various modules and PC analyses of gene expression get at this question?

There were some places in the methods of the preprint that required more information to properly evaluate. For example, more information should be provided on lines 664-668 about how G, E, and GxE effects were established, especially since this is so central to this study. What programs/software (R? SAS? Other?) were used for these analyses? If R, how were the ANOVAs/models fit? What type of ANOVA was used? How exactly was significance determined for each term? Which effects were considered fixed and which were random? If the goal was to fit mixed models, why not use an approach like voom-limma (Law et al. 2014 Genome Biology)? More details should also be added to lines 688-709 about these analyses, including what software/programs were used for these analyses.

One thing that I found a bit confusing throughout was the intermixing of different terms and types of selection. In particular, there seemed to be some inconsistencies with the usage of quantitative genetics terms for selection (e.g. directional, stabilizing) vs molecular evolution terms for selection (e.g. positive, purifying). I would encourage the authors to think carefully about what they mean by each of these terms and make sure that those definitions are consistently applied here.

It would be useful to clarify the reasons for the inherent bias in the detection of conditional neutrality (CN) and antagonistic pleiotropy (AP; Lines 187-196). It is also not clear to me what the authors did to deal with the bias in terms of adjusting P-value thresholds for CN and AP the way it is currently written. Further, I found the discussion of antagonistic pleiotropy and conditional neutrality to be a bit confusing for a couple of reasons, especially around lines 489-491. First of all, does it really make sense to contrast gene expression versus local adaptation, when lots of local adaptation likely involves changes in gene expression? Second, the implication that antagonistic pleiotropy is more common for local adaptation than the results found in this study seems questionable. Conditional neutrality appears to be more common for local adaptation as well: see Table 2 of Wadgymar et al. 2017 Methods in Ecology and Evolution. That all said, it is always difficult to conclude that there are no trade-offs (antagonistic pleiotropy) for a particular locus, as the detecting trade-offs may only manifest in some years and not others and can require large sample sizes if they are subtle in effect.

Reviewer #2 (Public Review):

The authors investigate the gene expression variation in a rice diversity panel under normal and saline growth conditions to gain insight into the underlying molecular adaptive response to salinity. They present a convincing case to demonstrate that environmental stress can induce selective pressure on gene expression, which is in agreement to their earlier study (Groen et al, 2020). The data seems to be a good fit for their study and overall the analytic approach is robust.

(1) The work started by investigating the effect of genotype and their interaction at each transcript level using 3'-end-biased mRNA sequencing, and detecting a wide-spread GXE effect. Later, using the total filled grain number as a proxy of fitness, they estimated the strength of selection on each transcript and reported stronger selective pressure in a saline environment. However, this current framework relies on precise estimation of fitness and, therefore can be sensitive to the choice of fitness proxy.

(2) Furthermore, the authors decomposed the genetic architecture of expression variation into cis- and trans-eQTL in each environment separately and reported more unique environment-specific trans-eQTLs than cis-. The relative contribution of cis- and trans-eQTL depends on both the abundance and effect size. I wonder why the latter was not reported while comparing these two different genetic architectures. If the authors were to compare the variation explained by these two categories of eQTL instead of their frequency, would the inference that trans-eQTLs are primarily associated with expression variation still hold?

(3) Next, the authors investigated the relationship between cis- and trans-eQTLs at the transcript level and revealed an excess of reinforcement over the compensation pattern. Here, I struggle to understand the motivation for testing the relationship by comparing the effect of cis-QTL with the mean effect of all trans-eQTLs of a given transcript. My concern is that taking the mean can diminish the effect of small trans-eQTLs potentially biasing the relationship towards the large-effect eQTLs.

Reviewer #3 (Public Review):

In this work, the authors conducted a large-scale field trial of 130 indica accessions in normal vs. moderate salt stress conditions. The experiment consists of 3 replicates for each accession in each treatment, making it 780 plants in total. Leaf transcriptome, plant traits, and final yield were collected. Starting from a quantitative genetics framework, the authors first dissected the heritability and selection forces acting on gene expression. After summarizing the selection force acting on gene expression (or plant traits) in each environment, the authors described the difference in gene expression correlation between environments. The final part consists of eQTL investigation and categorizing cis- and trans-effects acting on gene expression.

Building on the group's previous study and using a similar methodology (Groen et al. 2020, 2021), the unique aspect of this study is in incorporating large-scale empirical field works and combining gene expression data with plant traits. Unlike many systems biology studies, this study strongly emphasizes the quantitative genetics perspective and investigates the empirical fitness effects of gene expression data. The large amounts of RNAseq data (one sample for each plant individual) also allow heritability calculation. This study also utilizes the population genetics perspective to test for traces of selection around eQTL. As there are too many genes to fit in multiple regression (for selection analysis) and to construct the G-matrix (for breeder's equation), grouping genes into PCs is a very good idea.

Building on large amounts of data, this study conducted many analyses and described some patterns, but a central message or hypothesis would still be necessary. Currently, the selection analysis, transcript correlation structure change, and eQTL parts seem to be independent. The manuscript currently looks like a combination of several parallel works, and this is reflected in the Results, where each part has its own short introduction (e.g., 185-187, 261-266, 349-353). It would be great to discuss how these patterns observed could be translated to larger biological insights. On a related note, since this and the previous studies (focusing on dry-wet environments) use a similar methodology, one would also wonder what the conclusions from these studies would be. How do they agree or disagree with each other?

Many analyses were done separately for each environment, and results from these two environments are listed together for comparison. Especially for the eQTL part, no specific comparison was discussed between the two environments. It would be interesting to consider whether one could fit the data in more coherent models specifically modeling the X-by-environment effects, where X might be transcripts, PCs, traits, transcript-transcript correlation, or eQTLs.

As stated, grouping genes into PCs is a good idea, but although in theory, the PCs are orthogonal, each gene still has some loadings on each PC (ie. each PC is not controlled by a completely different set of genes). Another possibility is to use any gene grouping method, such as WGCNA, to group genes into modules and use the PC1 of each module. There, each module would consist of completely different sets of genes, and one would be more likely to separate the biological functions of each module. I wonder whether the authors could discuss the pros and cons of these methods.

Reviewer #4 (Public Review):

The manuscript examines how patterns of selection on gene expression differ between a normal field environment and a field environment with elevated salinity based on transcript abundances obtained from leaves of a diverse panel of rice germplasm. In addition, the manuscript also maps expression QTL (eQTL) that explains variation in each environment. One highlight from the mapping is that a small group of trans-mapping regulators explains some gene expression variation for large sets of transcripts in each environment. The overall scope of the datasets is impressive, combining large field studies that capture information about fecundity, gene expression, and trait variation at multiple sites. The finding related to patterns indicating increased LD among eQTLs that have cis-trans compensatory or reinforcing effects is interesting in the context of other recent work finding patterns of epistatic selection. However, other analyses in the manuscript are less compelling or do not make the most of the value of collected data. Revisions are also warranted to improve the precision with which field-specific terminology is applied and the language chosen when interpreting analytical findings.

Selection of gene expression:<br /> One strength of the dataset is that gene expression and fecundity were measured for the same genotypes in multiple environments. However, the selection analyses are largely conducted within environments. The addition of phenotypic selection analyses that jointly analyze gene expression across environments and or selection on reaction norms would be worthwhile.

Gene expression trade-offs:<br /> The terminology and possibly methods involved in the section on gene expression trade-offs need amendment. I specifically recommend discontinuing reference to the analysis presented as an analysis of antagonistic pleiotropy (rather than more general trade-offs) because pleiotropy is defined as a property of a genotype, not a phenotype. Gene expression levels are a molecular phenotype, influenced by both genotype and the environment. By conducting analyses of selection within environments as reported, the analysis does not account for the fact that the distribution of phenotypic values, the fitness surface, or both may differ across environments. Thus, this presents a very different situation than asking whether the genotypic effect of a QTL on fitness differs across environments, which is the context in which the contrasting terms antagonistic pleiotropy and conditional neutrality have been traditionally applied. A more interesting analysis would be to examine whether the covariance of phenotype with fitness has truly changed between environments or whether the phenotypic distribution has just shifted to a different area of a static fitness surface.

Biological processes under selection / Decoherence: PCs are likely not the most ideal way to cluster genes to generate consolidated metrics for a selection gradient analysis. Because individual genes will contribute to multiple PCs, the current fractional majority-rule method applied to determine whether a PC is under direct or indirect selection for increased or decreased expression comes across as arbitrary and with the potential for double-counting genes. A gene co-expression network analysis could be more appropriate, as genes only belong to one module and one can examine how selection is acting on the eigengene of a co-expression module. Building gene co-expression modules would also provide a complementary and more concrete framework for evaluating whether salinity stress induces "decoherence" and which functional groups of genes are most impacted.

Selection of traits:<br /> Having paired organismal and molecular trait data is a strength of the manuscript, but the organismal trait data are underutilized. The manuscript as written only makes weak indirect inferences based on GO categories or assumed gene functions to connect selection at the organismal and molecular levels. Stronger connections could be made for instance by showing a selection of co-expression module eigengene values that are also correlated with traits that show similar patterns of selection, or by demonstrating that GWAS hits for trait variation co-localize to cis-mapping eQTL.

Genetic architecture of gene expression variation:<br /> The descriptive statistics of the eQTL analysis summarize counts of eQTLs observed in each environment, but these numbers are not broken down to the molecular trait level (e.g., what are the median and range of cis- and trans-eQTLs per gene). In addition, genetic architecture is a combination of the numbers and relative effect sizes of the QTLs. It would be useful to provide information about the relative distributions of phenotypic variance explained by the cis- vs. trans- eQTLs and whether those distributions vary by environment. The motivation for examining patterns of cis-trans compensation specifically for the results obtained under high salinity conditions is unclear to me. If the lines sampled have predominantly evolved under low salinity conditions and the hypothesis being evaluated relates to historical experience of stabilizing selection, then my intuition is that evaluating the eQTL patterns under normal conditions provides the more relevant test of the hypothesis.

Author response:

Reviewer #1:

(1) Clarification of Novelty and Contribution:

- We agree that the novelty of our study could have been better articulated. We will more clearly define the specific gaps in knowledge our study addresses. We will also clarify the novelty in our analysis of the correlational structure of gene expression under stress.

(2) Methodological Details:

- We acknowledge the need for additional detail in the methods section regarding the estimation of G, E, and GxE effects. We will expand this section to include the software used (R), the specific ANOVA models applied, and how significance was determined. We will also clarify which effects were treated as fixed or random effects.

(3) Terminology Consistency:

- We will thoroughly review the manuscript to ensure consistent use of selection-related terminology. This will involve distinguishing between quantitative genetics terms (e.g., irectional, stabilizing) and molecular evolution terms (e.g., positive, purifying) to avoid any confusion.

(4) Bias in Conditional Neutrality and Antagonistic Pleiotropy:

- We appreciate the suggestion to clarify the discussion around conditional neutrality (CN) and antagonistic pleiotropy (AP). We will elaborate on the inherent bias in detecting CN and P and specify how we adjusted P-value thresholds. Additionally, we will try to refine the discussion to address the concerns raised about the comparison of gene expression and local adaptation, incorporating relevant literature.

Reviewer #2:

(1) Sensitivity of Fitness Proxy:

- We acknowledge the limitations of using the total filled grain number as a fitness proxy. We will include a discussion on the potential sensitivity of our results to this choice.

(2) Cis- and trans-eQTL Contributions:

- We appreciate the suggestion to report effect sizes in addition to the frequency of cis- and trans-eQTLs. We will incorporate this into our analysis and discuss whether our conclusions regarding the predominance of trans-eQTLs in expression variation hold when considering effect sizes.

(3) Cis-Trans Relationship Analysis:

- Since we wanted to estimate compensating vs. reinforcing effects, this essentially entails identifying genes that have opposing directionality of cis and trans-effects. To get the total trans-effect we decided to take the mean effect of trans-eQTLs. This mean was only used to identify the compensating/reinforcing genes and although the mean effects diminishes the effect of small trans-eQTLs, this metric was not used in downstream analyses.

Reviewer #3:

(1) Integration of Analyses:

- We acknowledge that the manuscript currently presents some analyses in a somewhat independent manner. Although it would be ideal to have a central hypothesis/message, our study is meant to broadly outline the various responses and fitness effects of salinity stress on rice. Throughout the manuscript, we have also included comparisons between our findings and that of our previous studies on drought stress to highlight any consistent themes or novel insights.

(2) X-by-Environment Effects:

- We do plan to consider fitting models that explicitly incorporate X-by-environment interactions to provide a more detailed understanding of the genetics of plasticity between the two environments, but it is beyond the scope of this paper. This will be explored in a separate report.

(3) Gene Grouping Methods:<br /> - We will try to discuss the pros and cons of using PCA versus gene co-expression network analysis (e.g., WGCNA) for grouping genes. We will also explore applying WGCNA in our analysis to see if it offers any additional insights or clarity.

Reviewer #4:

(1) Selection Analysis Across Environments:

- We do plan to consider fitting models that explicitly incorporate G×E interactions to provide a more detailed understanding of the genetics of plasticity between the two environments, but it is beyond the scope of this paper. This will be explored in a separate report.

(2) Gene Expression Trade-Offs Terminology:

- We will revise our terminology to better reflect the nature of the trade-offs observed, and explore variation in covariance between phenotype and fitness between the two environments.

(3) Biological Processes and Decoherence:

- We will explore applying WGCNA in our analysis to see if it offers any additional insights or clarity.

(4) Underutilization of Organismal Traits:

- We did perform GWAS for all the traits measured in both environments, but did not find any significant hits. We will examine whether selection of co-expression modules are correlated with the traits, and may incorporate it in our manuscript depending on the results.

(5) Detailed eQTL Analysis:

- We will expand our eQTL analysis to include detailed statistics at the molecular trait level, including the phenotypic variance explained by cis- and trans-eQTLs and how these vary by environment.

Although we focus on salinity conditions in our cis-trans compensation analysis in the main results, we have provided comparisons for all our eQTL analyses between normal and salinity conditions in the main text (with figures as supplementary).<br /> We are confident that these revisions will significantly strengthen our manuscript and address the concerns raised by the reviewers. We look forward to submitting a revised version that better communicates the significance and robustness of our findings.<br /> Thank you again for your valuable feedback.

eLife assessment

This study provides new insights into the expression profile of ILCs that demonstrate a history of RAG expression. It examines in part the potential intrinsic regulation of RAG expression and seeks to understand how the epigenetic state of ILCs is established, although a full understanding of intrinsic factors is incomplete. The work provides an important molecular dataset, and with further strengthening of the understanding of intrinsic regulation, this paper would be of interest more broadly to cell biologists seeking to understand immune cell development.

Reviewer #1 (Public Review):

The study starts with the notion that in an AD-like disease model, ILC2s in the Rag1 knock-out were expanded and contained relatively more IL-5+ and IL-13+ ILC2s. This was confirmed in the Rag2 knock-out mouse model.

By using a chimeric mouse model in which wild-type knock-out splenocytes were injected into irradiated Rag1 knock-out mice, it was shown that even though the adaptive lymphocyte compartment was restored, there were increased AD-like symptoms and increased ILC2 expansion and activity. Moreover, in the reverse chimeric model, i.e. injecting a mix of wild-type and Rag1 knock-out splenocytes into irradiated wild-type animals, it was shown that the Rag1 knock-out ILC2s expanded more and were more active. Therefore, the authors could conclude that the RAG1 mediated effects were ILC2 cell-intrinsic.

Subsequent fate-mapping experiments using the Rag1Cre;reporter mouse model showed that there were indeed RAGnaïve and RAGexp ILC2 populations within naïve mice. Lastly, the authors performed multi-omic profiling, using single-cell RNA sequencing and ATAC-sequencing, in which a specific gene expression profile was associated with ILC2. These included well-known genes but the authors notably also found expression of Ccl1 and Ccr8 within the ILC2. The authors confirmed their earlier observations that in the RAGexp ILC2 population, the Th2 regulome was more suppressed, i.e. more closed, compared to the RAGnaïve population, indicative of the suppressive function of RAG on ILC2 activity. I do agree with the authors' notion that the main weakness was that this study lacks the mechanism by which RAG regulates these changes in ILC2s.

The manuscript is very well written and easy to follow, and the compelling conclusions are well supported by the data. The experiments are meticulously designed and presented. I wish to commend the authors for the study's quality.

Even though the study is compelling and well supported by the presented data, some additional context could increase the significance:

(1) The presence of the RAGnaïve and RAGexp ILC2 populations raises some questions on the (different?) origin of these populations. It is known that there are different waves of ILC2 origin (most notably shown in the Schneider et al Immunity 2019 publication, PMID 31128962). I believe it would be very interesting to further discuss or possibly show if there are different origins for these two ILC populations.

Several publications describe the presence and origin of ILC2s in/from the thymus (PMIDs 33432227 24155745). Could the authors discuss whether there might be a common origin for the RAGexp ILC2 and Th2 cells from a thymic lineage? If true that the two populations would be derived from different populations, e.g. being the embryonic (possibly RAGnaïve) vs. adult bone marrow/thymus (possibly RAGexp), this would show a unique functional difference between the embryonic derived ILC2 vs. adult ILC2.

(2) On line 104 & Figures 1C/G etc. the authors describe that in the RAG knock-out ILC2 are relatively more abundant in the lineage negative fraction. On line 108 they further briefly mentioned that this observation is an indication of enhanced ILC2 expansion. Since the study includes an extensive multi-omics analysis, could the authors discuss whether they have seen a correlation of RAG expression in ILC2 with regulation of genes associated with proliferation, which could explain this phenomenon?

Reviewer #2 (Public Review):

Summary:

The study by Ver Heul et al., investigates the consequences of RAG expression for type 2 innate lymphoid cell (ILC2) function. RAG expression is essential for the generation of the receptors expressed by B and T cells and their subsequent development. Innate lymphocytes, which arise from the same initial progenitor populations, are in part defined by their ability to develop in the absence of RAG expression. However, it has been described in multiple studies that a significant proportion of innate lymphocytes show a history of Rag expression. In compelling studies several years ago, members of this research team revealed that early Rag expression during the development of Natural Killer cells (Karo et al., Cell 2014), the first described innate lymphocyte, had functional consequences.

Here, the authors revisit this topic, a worthwhile endeavour given the broad history of Rag expression within all ILCs and the common use of RAG-deficient mice to specifically assess ILC function. Focusing on ILC2s and utilising state-of-the-art approaches, the authors sought to understand whether early expression of Rag during ILC2 development had consequences for activity, fitness, or function. Having identified cell-intrinsic effects in vivo, the authors investigated the causes of this, identifying epigenetic changes associated with the accessibility genes associated with core ILC2 functions.

The manuscript is well written and does an excellent job of supporting the reader through reasonably complex transcriptional and epigenetic analyses, with considerate use of explanatory diagrams. Overall I think that the conclusions are fair, the topic is thought-provoking, and the research is likely of broad immunological interest. I think that the extent of functional data and mechanistic insight is appropriate.

Strengths:

- The logical and stepwise use of mouse models to first demonstrate the impact on ILC2 function in vivo and a cell-intrinsic role. Initial analyses show enhanced cytokine production by ILC2 from RAG-deficient mice. Then through two different chimeric mice (including BM chimeras), the authors convincingly show this is cell intrinsic and not simply as a result of lymphopenia. This is important given other studies implicating enhanced ILC function in RAG-/- mice reflect altered competition for resources (e.g. cytokines).

- Use of Rag expression fate mapping to support analyses of how cells were impacted - this enables a robust platform supporting subsequent analyses of the consequences of Rag expression for ILC2.

- Use of snRNA-seq supports gene expression and chromatin accessibility studies - these reveal clear differences in the data sets consistent with altered ILC2 function.

- Convincing evidence of epigenetic changes associated with loci strongly linked to ILC2 function. This forms a detailed analysis that potentially helps explain some of the altered ILC2 functions observed in ex vivo stimulation assays.

- Provision of a wealth of expression data and bioinformatics analyses that can serve as valuable resources to the field.

Weaknesses:

- Lack of insight into precisely how early RAG expression mediates its effects, although I think this is beyond the scale of this current manuscript. Really this is the fundamental next question from the data provided here.

- The epigenetic analyses provide evidence of differences in the state of chromatin, but there is no data on what may be interacting or binding at these sites, impeding understanding of what this means mechanistically.

- Focus on ILC2 from skin-draining lymph nodes rather than the principal site of ILC2 activity itself (the skin). This may well reflect the ease at which cells can be isolated from different tissues.

- Comparison with ILC2 from other sites would have helped to substantiate findings and compensate for the reliance on data on ILC2 from skin-draining lymph nodes, which are not usually assessed amongst ILC2 populations.

- The studies of how ILC2 are impacted are a little limited, focused exclusively on IL-13 and IL-5 cytokine expression.

Reviewer #3 (Public Review):

In this study, Ver Heul et al. investigate the role of RAG expression in ILC2 functions. While RAG genes are not required for the development of ILCs, previous studies have reported a history of expression in these cells. The authors aim to determine the potential consequences of this expression in mature cells. They demonstrate that ILC2s from RAG1 or RAG2 deficient mice exhibit increased expression of IL-5 and IL-13 and suggest that these cells are expanded in the absence of RAG expression. However, it is unclear whether this effect is due to a direct impact of RAG genes or a consequence of the lack of T and B cells in this condition. This ambiguity represents a key issue with this study: distinguishing the direct effects of RAG genes from the indirect consequences of a lymphopenic environment.

The authors focus their study on ILC2s found in the skin-draining lymph nodes, omitting analysis of tissues where ILC2s are more enriched, such as the gut, lungs, and fat tissue. This approach is surprising given the goal of evaluating the role of RAG genes in ILC2s across different tissues. The study shows that ILC2s derived from RAG-/- mice are more activated than those from WT mice, and RAG-deficient mice show increased inflammation in an atopic dermatitis (AD)-like disease model. The authors use an elegant model to distinguish ILC2s with a history of RAG expression from those that never expressed RAG genes. However, this model is currently limited to transcriptional and epigenomic analyses, which suggest that RAG genes suppress the type 2 regulome at the Th2 locus in ILC2s.

The authors report a higher frequency of ILC2s in RAG-/- mice in skin-draining lymph nodes, which is expected as these mice lack T and B cells, leading to ILC expansion. Previous studies have reported hyper-activation of ILCs in RAG-deficient mice, suggesting that this is not necessarily an intrinsic phenomenon. For example, RAG-/- mice exhibit hyperphosphorylation of STAT3 in the gut, leading to hyperactivation of ILC3s. This study does not currently provide conclusive evidence of an intrinsic role of RAG genes in the hyperactivation of ILC2s. The splenocyte chimera model is artificial and does not reflect a normal environment in tissues other than the spleen. Similarly, the mixed BM model does not demonstrate an intrinsic role of RAG genes, as RAG1-/- BM cells cannot contribute to the B and T cell pool, leading to an expected expansion of ILC2s. As the data are currently presented it is expected that a proportion of IL-5-producing cells will come from the RAG1-/- BM.

Overall, the level of analysis could be improved. Total cell numbers are not presented, the response of other immune cells to IL-5 and IL-13 (except the eosinophils in the splenocyte chimera mice) is not analyzed, and the analysis is limited to skin-draining lymph nodes.

The authors have a promising model in which they can track ILC2s that have expressed RAG or not. They need to perform a comprehensive characterization of ILC2s in these mice, which develop in a normal environment with T and B cells. Approximately 50% of the ILC2s have a history of RAG expression. It would be valuable to know whether these cells differ from ILC2s that never expressed RAG, in terms of proliferation and expression of IL-5 and IL-13. These analyses should be conducted in different tissues, as ILC2s adapt their phenotype and transcriptional landscape to their environment. Additionally, the authors should perform their AD-like disease model in these mice.

The authors provide a valuable dataset of single-nuclei RNA sequencing (snRNA-seq) and ATAC sequencing (snATAC-seq) from RAGexp (RAG fate map-positive) and RAGnaïve (RAG fate map-negative) ILC2s. This elegant approach demonstrates that ILC2s with a history of RAG expression are epigenomically suppressed. However, key genes such as IL-5 and IL-13 do not appear to be differentially regulated between RAGexp and RAGnaïve ILC2s according to Table S5. Although the authors show that the regulome activity of IL-5 and IL-13 is decreased in RAGexp ILC2s, how do the authors explain that these genes are not differentially expressed between the RAGexp and RAGnaïve ILC2? I think that it is important to validate this in vivo.

eLife assessment

This study provides a valuable characterization of individual sarcomere's contractility and synchrony in spontaneously beating cardiomyocytes as a function of substrate stiffness. The authors, however, provide an incomplete explanation for the observed heterogeneous and stochastic dynamics, so that the work remains mainly descriptive. The work will be of interest to scientists working on muscle biophysics, nonlinear dynamics, and synchronization phenomena in biological systems.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors experimentally demonstrated the heterogeneous behavior of sarcomeres in cardiomyocytes and that a stochastic component exists in their contractile activity, which cancels out at the level of myofibrils.

Strengths:

The experiments and data analysis are robust and valid. With very good statistics and unbiased methods, they show cellular activity at the individual level and highlight the heterogeneity between biological networks. The similarity of the results to the study cited in [24] demonstrates the validity of the in vitro setup for answering these questions and the feasibility of such in-vitro systems to extend our knowledge of physiology.

Weaknesses:

Compared to the current literature ([24]), the study does not show a high degree of innovation. It mainly confirms what has been established in the past. The authors complemented the published experiments by developing an in vitro setup with stem cells and by changing the stiffness of the substrate to simulate pathological conditions. However, the experiments they performed do not allow them to explain more than the study in [24], and the conclusions of their study are based on interpretation and speculation about the possible mechanism underlying the observations.

Reviewer #2 (Public Review):

Summary:

Sarcomeres, the contractile units of skeletal and cardiac muscle, contract in a concerted fashion to power myofibril and thus muscle fiber contraction.

Muscle fiber contraction depends on the stiffness of the elastic substrate of the cell, yet it is not known how this dependence emerges from the collective dynamics of sarcomeres. Here, the authors analyze the contraction time series of individual sarcomeres using live imaging of fluorescently labeled cardiomyocytes cultured on elastic substrates of different stiffness. They find that reduced collective contractility of muscle fibers on unphysiologically stiff substrates is partially explained by a lack of synchronization in the contraction of individual sarcomeres.

This lack of synchronization is at least partially stochastic, consistent with the notion of a tug-of-war between sarcomeres on stiff sarcomeres. A particular irregularity of sarcomere contraction cycles is 'popping', the extension of sarcomeres beyond their rest length. The statistics of 'popping' suggest that this is a purely random process.

Strengths:

This study thus marks an important shift of perspective from whole-cell analysis towards an understanding of the collective dynamics of coupled, stochastic sarcomeres.

Weaknesses:

Further insight into mechanisms could be provided by additional analyses and/or comparisons to mathematical models.

Reviewer #3 (Public Review):

Summary:

The manuscript of Haertter and coworkers studied the variation of length of a single sarcomere and the response of microfibrils made by sarcomeres of cardiomyocytes on soft gel substrates of varying stiffnesses.

The measurements at the level of a single sarcomere are an important new result of this manuscript. They are done by combining the labeling of the sarcomeres z line using genetic manipulation and a sophisticated tracking program using machine learning. This single sarcomere analysis shows strong heterogeneities of the sarcomeres that can show fast oscillations not synchronized with the average behavior of the cell<br /> and what the authors call popping events which are large amplitude oscillations. Another important result is the fact that cardiomyocyte contractility decreases with the substrate stiffness although the properties of single sarcomeres do not seem to depend on substrate stiffness.

The authors suggest that the cardiomyocyte cell behavior is dominated by sarcomere heterogeneity. They show that the heterogeneity between sarcomeres is stochastic and that the contribution of static heterogeneity (such as composition differences between sarcomeres)<br /> is small.

Strengths:

All the results are to my knowledge new and original and deserve attention.

Weaknesses:

However, I find the manuscript a bit frustrating because the authors only give very qualitative explanations of the phenomena that they observe. They mention that popping could be explained by a nonlinear force-velocity relation of the sarcomere leading to a rapid detachment of all motors. However, they do not explicitly provide a theoretical description. How would the popping depend on the parameters and in particular on the substrate stiffness? Would the popping statistics be affected by the stiffness? It is also not clear to me how the dependence on the soft gel stiffness of the cardiomyocyte cell can be explained by the stochasticity of the sarcomere properties. Can any of the results found by the authors be explained by existing theories of cardiomyocytes? The only one I know is that of Safran and coworkers.

I also found the paper very difficult to read. The authors should perhaps reorganize the structure of the presentation in order to highlight what the new and important results are.

eLife assessment

This study demonstrates a novel role for SIRT4; a mitochondrial deacetylase, shown to translocate into nuclei where it regulates RNA alternative splicing by modulating U2AF2 and the gene expression of CCN2 in tubular cells in response to TGF-β. This fundamental work substantially advances our understanding of kidney fibrosis development and offers a potential therapeutic approach. The evidence supporting the conclusions of a SIRT4-U2AF2-CCN2 axis activated by TGF-β is compelling and adds a new layer of complexity to the pathogenesis of chronic kidney disease.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Yang et al report a novel regulatory role of SIRT4 in the progression of kidney fibrosis. The authors showed that in the fibrotic kidney, SIRT4 exhibited an increased nuclear localization. Deletion of Sirt4 in renal tubule epithelium attenuated the extent of kidney fibrosis following injury, while overexpression of SIRT4 aggravates kidney fibrosis. Employing a battery of in vitro and in vivo experiments, the authors demonstrated that SIRT4 interacts with U2AF2 in the nucleus upon TGF-β1 stimulation or kidney injury and deacetylates U2AF2 at K413, resulting in elevated CCN2 expression through alternative splicing of Ccn2 gene to promote kidney fibrosis. The authors further showed that the translocation of SIRT4 is through the BAX/BAK pore complex and is dependent on the ERK1/2-mediated phosphorylation of SIRT4 at S36, and consequently the binding of SIRT4 to importin α1. This fundamental work substantially advances our understanding of the progression of kidney fibrosis and uncovers a novel SIRT4-U2AF2-CCN2 axis as a potential therapeutic target for kidney fibrosis.

Strengths:

Overall, this is an extensive, well-performed study. The results are convincing, and the conclusions are mostly well supported by the data. The message is interesting to a wider community working on kidney fibrosis, protein acetylation, and SIRT4 biology.

Weaknesses:

The manuscript could be further strengthened if the authors could address a few points listed below:

(1) In the results part 3.9, an in vitro deacetylation assay employing recombinant SIRT4 and U2AF2 should be included to support the conclusion that SIRT4 is a deacetylase of U2AF2. Similarly, an in vitro binding assay can be included to confirm whether SIRT4 and U2AF2 are directly interacted.

(2) In Figure 6D, the Western Blot data using U2AF2-K453Q is confusing and is quite disconnected from the rest of the data and not explained. This data can be removed or explained why U2AF2-K453Q is employed here.

(3) Although ERK inhibitor U0126 blocked the nuclear translocation of SIRT4 in vivo, have the authors checked whether treatment with U0126 could affect the expression of kidney fibrosis markers in UUO mice?

(4) The format of gene and protein abbreviations in the manuscript should be standardized.

(5) There are a few grammar issues throughout the manuscript. The English/grammar could be stronger, thus improving the overall accessibility of the science to readers.

Reviewer #2 (Public Review):

Summary:

This manuscript presents a novel and significant investigation into the role of SIRT4 For CCN2 expression in response to TGF-β by modulating U2AF2-mediated alternative splicing and its impact on the development of kidney fibrosis.

Strengths:

The authors' main conclusion is that SIRT4 plays a role in kidney fibrosis by regulating CCN2 expression via pre-mRNA splicing. Additionally, the study reveals that SIRT4 translocates from the mitochondria to the cytoplasm through the BAX/BAK pore under TGF-β stimulation. In the cytoplasm, TGF-β activated the ERK pathway and induced the phosphorylation of SIRT4 at Ser36, further promoting its interaction with importin α1 and subsequent nuclear translocation. In the nucleus, SIRT4 was found to deacetylate U2AF2 at K413, facilitating the splicing of CCN2 pre-mRNA to promote CCN2 protein expression. Overall, the findings are fully convincing. The current study, to some extent, shows potential importance in this field. 

Weaknesses:

(1) Exosomes containing anti-SIRT4 antibodies were found to effectively mitigate UUO-induced kidney fibrosis in mice. While the protein loading capacity and loading methods were not mentioned.

(2) The method section is incomplete, and many methods like cell culture, cell transfection, gene expression profiling analysis, and splicing analysis, were not introduced in detail.

(3) The authors should compare their results with previous studies and mention clearly how their work is important in comparison to what has already been reported in the Discussion section.

Reviewer #3 (Public Review):

Summary:

Yang et al reported in this paper that TGF-beta induces SIRT4 activation, TGF-beta activated SIRT4 then modulates U2AF2 alternative splicing, U2AF2 in turn causes CCN2 for expression. The mechanism is described as this: mitochondrial SIRT4 transport into the cytoplasm in response to TGF-β stimulation, phosphorylated by ERK in the cytoplasm, and pathway and then undergo nuclear translocation by forming the complex with importin α1. In the nucleus, SIRT4 can then deacetylate U2AF2 at K413 to facilitate the splicing of CCN2 pre-mRNA to promote CCN2 protein expression. Moreover, they used exosomes to deliver Sirt4 antibodies to mitigate renal fibrosis in a mouse model. TGF-beta has been widely reported for its role in fibrosis induction.

Strengths:

TGF-beta induction of SIRT4 translocation from mitochondria to nuclei for epigenetics or gene regulation remains largely unknown. The findings presented here that SIRT4 is involved in U2AF2 deacetylation and CCN2 expression are interesting.

Weaknesses:

SIRT4 plays a critical role in mitochondria involved in respiratory chain reaction. This role of SIRT4 is critically involved in many cell functions. It is hard to rule out such a mitochondrial activity of SIRT4 in renal fibrosis. Moreover, the major concern is what kind of message mitochondrial SIRT4 proteins receive from TGF-beta. Although nuclear SIRT4 is increased in response to TNF treatment, it is likely de novo synthesized SIRT4 proteins can also undergo nuclear translocation upon cytokine stimulation. TGF-beta-induced mitochondrial calcium uptake and acetyl-CoA should be evaluated for calcium and acetyl-CoA may contribute to the gene expression regulation in nuclei.

eLife assessment

Zhao et al. report valuable adverse effects on cell proliferation, differentiation and gene expression, possibly linked to reduced binding activity of the transcription factor GTF2IRD1 to the transthyretin (TTR) promoter, in a human forebrain organoid model of Williams Syndrome (WS). The authors provide incomplete evidence of the effects of GTF2IRD1, a mutated gene in WS, on altering MAPK/ERK pathway activity, a well-recognized target in cell proliferation.

Reviewer #1 (Public Review):

Summary:

Zhao et al. used the human forebrain organoid model, transgenic mice model, and embryonic neural progenitor cells to investigate the mutation previously identified in Williams Syndrome. They found abnormal proliferation and differentiation induced by this mutation, as well as altered expression profiles corresponding with aberrant cell clusters. This is regulated through the binding of GTF2IRD1 to transthyretin (TTR) promoter regions and tested on three models mentioned above on neurodevelopmental deficits.

Strengths:

Authors have applied both cell culture, organoid culture and in vivo model to test the previously reported mutation found in Williams Syndrome. They investigated cell behavior including proliferation and differentiation, while using the NGS technique to identify potential signaling pathways that are highly involved and can serve as a candidate to save the phenotype.

Reviewer #2 (Public Review):

Summary:

The study by Xingsen Zhao et al on "A human forebrain organoid model reveals the essential function of GTF2IRD1-TTR-ERK axis for the neurodevelopmental deficits of Williams Syndrome" presents a forebrain organoid model for WS and has identified defects in neurogenesis. The authors have performed scRNAseq from these patients' derived forebrain organoids showing upregulation expression in genes related to cell proliferation while genes involved in neuronal differentiation were downregulated. The major findings presented in this study are an increase in the size of SOX2+ ventricular zone in WS forebrain organoids with an altered developmental trajectory and aberrant excitatory neurogenesis. The study also presents evidence that transthyretin (TTR) has a reduced expression in WS organoids, and its expression is regulated by the transcription factor -GTF2IRD1. The authors then go on identity mechanistic details of TTR function on MAPK/ERK pathway which has been known to be involved in brain development. Overall, this is a well-constructed study revealing the function of one of the key genes that is deleted in WS and provides novel insights into mechanisms underlying the abnormal neurogenesis in WS brain.

Strengths:

WS patients have neurocognitive disorders which most likely stem from defects in early neurodevelopment. This study has investigated a WS forebrain organoid model with scRNAseq and identified differences in cell proliferation and differentiation. This study has presented some new evidence regarding the function and regulation of TTR and its regulator GTF2IRD1 during brain development.

Weaknesses:

Though the evidence presented for the mechanism of action of TTR on the MAPK pathway is unclear and lacks depth. It would require identifying downstream targets of TTR and how it interacts with the MAPK pathway.

eLife assessment

The authors present a potentially useful approach of broad interest arguing that anterior cingulate cortex (ACC) tracks option values in decisions involving delayed rewards. The authors introduce the idea of a resource-based cognitive effort signal in ACC ensembles and link ACC theta oscillations to a resistance-based strategy. The evidence supporting these new ideas is incomplete and would benefit from additional detail and more rigorous analyses and computational methods.

Reviewer #1 (Public Review):

Summary:

Young (2.5 mo [adolescent]) rats were tasked to either press one lever for immediate reward or another for delayed reward. The task had a complex structure in which (1) the number of pellets provided on the immediate reward lever changed as a function of the decisions made, (2) rats were prevented from pressing the same lever three times in a row. Importantly, this task is very different from most intertemporal choice tasks which adjust delay (to the delayed lever), whereas this task held the delay constant and adjusted the number of 20 mg sucrose pellets provided on the immediate value lever.

Analyses are based on separating sessions into groups, but group membership includes arbitrary requirements and many sessions have been dropped from the analyses. Computational modeling is based on an overly simple reinforcement learning model, as evidenced by fit parameters pegging to the extremes. The neural analysis is overly complex and does not contain the necessary statistics to assess the validity of their claims.

Strengthes:

The task is interesting.

Weaknesses:

Behavior:

The basic behavioral results from this task are not presented. For example, "each recording session consisted of 40 choice trials or 45 minutes". What was the distribution of choices over sessions? Did that change between rats? Did that change between delays? Were there any sequence effects? (I recommend looking at reaction times.) Were there any effects of pressing a lever twice vs after a forced trial? This task has a very complicated sequential structure that I think I would be hard pressed to follow if I were performing this task. Before diving into the complex analyses assuming reinforcement learning paradigms or cognitive control, I would have liked to have understood the basic behaviors the rats were taking. For example, what was the typical rate of lever pressing? If the rats are pressing 40 times in 45 minutes, does waiting 8s make a large difference?

For that matter, the reaction time from lever appearance to lever pressing would be very interesting (and important). Are they making a choice as soon as the levers appear? Are they leaning towards the delay side, but then give in and choose the immediate lever? What are the reaction time hazard distributions?

It is not clear that the animals on this task were actually using cognitive control strategies on this task. One cannot assume from the task that cognitive control is key. The authors only consider a very limited number of potential behaviors (an overly simple RL model). On this task, there are a lot of potential behavioral strategies: "win-stay/lose-shift", "perseveration", "alternation", even "random choices" should be considered.

The delay lever was assigned to the "non-preferred side". How did side bias affect the decisions made?

The analyses based on "group" are unjustified. The authors compare the proportion of delayed to immediate lever press choices on the non-forced trials and then did k-means clustering on this distribution. But the distribution itself was not shown, so it is unclear whether the "groups" were actually different. They used k=3, but do not describe how this arbitrary number was chosen. (Is 3 the optimal number of clusters to describe this distribution?) Moreover, they removed three group 1 sessions with an 8s delay and two group 2 sessions with a 4s delay, making all the group 1 sessions 4s delay sessions and all group 2 sessions 8s delay sessions. They then ignore group 3 completely. These analyses seem arbitrary and unnecessarily complex. I think they need to analyze the data by delay. (How do rats handle 4s delay sessions? How do rats handle 6s delay sessions? How do rats handle 8s delay sessions?). If they decide to analyze the data by strategy, then they should identify specific strategies, model those strategies, and do model comparison to identify the best explanatory strategy. Importantly, the groups were session-based, not rat based, suggesting that rats used different strategies based on the delay to the delayed lever.

The reinforcement learning model used was overly simple. In particular, the RL model assumes that the subjects understand the task structure, but we know that even humans have trouble following complex task structures. Moreover, we know that rodent decision-making depends on much more complex strategies (model-based decisions, multi-state decisions, rate-based decisions, etc). There are lots of other ways to encode these decision variables, such as softmax with an inverse temperature rather than epsilon-greedy. The RL model was stated as a given and not justified. As one critical example, the RL model fit to the data assumed a constant exponential discounting function, but it is well-established that all animals, including rodents, use hyperbolic discounting in intertemporal choice tasks. Presumably this changes dramatically the effect of 4s and 8s. As evidence that the RL model is incomplete, the parameters found for the two groups were extreme. (Alpha=1 implies no history and only reacting to the most recent event. Epsilon=0.4 in an epsilon-greedy algorithm is a 40% chance of responding randomly.)

The authors do add a "dbias" (which is a preference for the delayed lever) term to the RL model, but note that it has to be maximal in the 4s condition to reproduce group 2 behavior, which means they are not doing reinforcement learning anymore, just choosing the delayed lever.

Neurophysiology:

The neurophysiology figures are unclear and mostly uninterpretable; they do not show variability, statistics or conclusive results.

As with the behavior, I would have liked to have seen more traditional neurophysiological analyses first. What do the cells respond to? How do the manifolds change aligned to the lever presses? Are those different between lever presses? Are there changes in cellular information (both at the individual and ensemble level) over time in the session? How do cellular responses differ during that delay while both levers are out, but the rats are not choosing the immediate lever?

Figure 3, for example, claims that some of the principal components tracked the number of pellets on the immediate lever ("ival"), but they are just two curves. No statistics, controls, or justification for this is shown. BTW, on Figure 3, what is the event at 200s?

I'm confused. On Figure 4, the number of trials seems to go up to 50, but in the methods, they say that rats received 40 trials or 45 minutes of experience.

At the end of page 14, the authors state that the strength of the correlation did not differ by group and that this was "predicted" by the RL modeling, but this statement is nonsensical, given that the RL modeling did not fit the data well, depended on extreme values. Moreover, this claim is dependent on "not statistically detectable", which is, of course, not interpretable as "not different".

There is an interesting result on page 16 that the increases in theta power were observed before a delayed lever press but not an immediate lever press, and then that the theta power declined after an immediate lever press. These data are separated by session group (again group 1 is a subset of the 4s sessions, group 2 is a subset of the 8s sessions, and group 3 is ignored). I would much rather see these data analyzed by delay itself or by some sort of strategy fit across delays. That being said, I don't see how this description shows up in Figure 6. What does Figure 6 look like if you just separate the sessions by delay?

Discussion:

Finally, it is unclear to what extent this task actually gets at the questions originally laid out in the goals and returned to in the discussion. The idea of cognitive effort is interesting, but there is no data presented that this task is cognitive at all. The idea of a resourced cognitive effort and a resistance cognitive effort is interesting, but presumably the way one overcomes resistance is through resource-limited components, so it is unclear that these two cognitive effort strategies are different.

The authors state that "ival-tracking" (neurons and ensembles that presumably track the number of pellets being delivered on the immediate lever - a fancy name for "expectations") "taps into a resourced-based form of cognitive effort", but no evidence is actually provided that keeping track of the expectation of reward on the immediate lever depends on attention or mnemonic resources. They also state that a "dLP-biased strategy" (waiting out the delay) is a "resistance-based form of cognitive effort" but no evidence is made that going to the delayed side takes effort.

The authors talk about theta synchrony, but never actually measure theta synchrony, particularly across structures such as amygdala or ventral hippocampus. The authors try to connect this to "the unpleasantness of the delay", but provide no measures of pleasantness or unpleasantness. They have no evidence that waiting out an 8s delay is unpleasant.

The authors hypothesize that the "ival-tracking signal" (the expectation of number of pellets on the immediate lever) "could simply reflect the emotional or autonomic response". Aside from the fact that no evidence for this is provided, if this were to be true, then, in what sense would any of these signals be related to cognitive control?

Reviewer #2 (Public Review):

Summary:

This manuscript explores the neuronal signals that underlie resistance vs resource-based models of cognitive effort. The authors use a delayed discounting task and computational models to explore these ideas. The authors find that the ACC strongly tracks value and time, which is consistent with prior work. Novel contributions include quantification of a resource-based control signal among ACC ensembles, and linking ACC theta oscillations to a resistance-based strategy.

Strengths:

The experiments and analyses are well done and have the potential to generate an elegant explanatory framework for ACC neuronal activity. The inclusion of local-field potential / spike-field analyses is particularly important because these can be measured in humans.

Weaknesses:

I had questions that might help me understand the task and details of neuronal analyses.

(1) The abstract, discussion, and introduction set up an opposition between resource and resistance-based forms of cognitive effort. It's clear that the authors find evidence for each (ACC ensembles = resource, theta=resistance?) but I'm not sure where the data fall on this dichotomy.<br /> a. An overall very simple schematic early in the paper (prior to the MCML model? or even the behavior) may help illustrate the main point.<br /> b. In the intro, results, and discussion, it may help to relate each point to this dichotomy.<br /> c. What would resource-based signals look like? What would resistance based signals look like? Is the main point that resistance-based strategies dominate when delays are short, but resource-based strategies dominate when delays are long?<br /> d. I wonder if these strategies can be illustrated? Could these two measures (dLP vs ival tracking) be plotted on separate axes or extremes, and behavior, neuronal data, LFP, and spectral relationships be shown on these axes? I think Figure 2 is working towards this. Could these be shown for each delay length? This way, as the evidence from behavior, model, single neurons, ensembles, and theta is presented, it can be related to this framework, and the reader can organize the findings.

(2) The task is not clear to me.<br /> a. I wonder if a task schematic and a flow chart of training would help readers.<br /> b. This task appears to be relatively new. Has it been used before in rats (Oberlin and Grahame is a mouse study)? Some history / context might help orient readers.<br /> c. How many total sessions were completed with ascending delays? Was there criteria for surgeries? How many total recording sessions per animal (of the 54?)<br /> d. How many trials completed per session (40 trials OR 45 minutes)? Where are there errors? These details are important for interpreting Figure 1.

(3) Figure 1 is unclear to me.<br /> a. Delayed vs immediate lever presses are being plotted - but I am not sure what is red, and what is blue. I might suggest plotting each animal.<br /> b. How many animals and sessions go into each data point?<br /> c. Table 1 (which might be better referenced in the paper) refers to rats by session. Is it true that some rats (2 and 8) were not analyzed for the bulk of the paper? Some rats appear to switch strategies, and some stay in one strategy. How many neurons come from each rat?<br /> d. Task basics - RT, choice, accuracy, video stills - might help readers understand what is going into these plots<br /> e. Does the animal move differently (i.e., RTs) in G1 vs. G2?

(4) I wasn't sure how clustered G1 vs. G2 vs G3 are. To make this argument, the raw data (or some axis of it) might help.<br /> a. This is particularly important because G3 appears to be a mix of G1 and G2, although upon inspection, I'm not sure how different they really are<br /> b. Was there some objective clustering criteria that defined the clusters?<br /> c. Why discuss G3 at all? Can these sessions be removed from analysis?

(5) The same applies to neuronal analyses in Fig 3 and 4<br /> a. What does a single neuron peri-event raster look like? I would include several of these.<br /> b. What does PC1, 2 and 3 look like for G1, G2, and G3?<br /> c. Certain PCs are selected, but I'm not sure how they were selected - was there a criteria used? How was the correlation between PCA and ival selected? What about PCs that don't correlate with ival?<br /> d. If the authors are using PCA, then scree plots and PETHs might be useful, as well as comparisons to PCs from time-shuffled / randomized data.

(6) I had questions about the spectral analysis<br /> a. Theta has many definitions - why did the authors use 6-12 Hz? Does it come from the hippocampal literature, and is this the best definition of theta?. What about other bands (delta - 1-4 Hz), theta (4-7 Hz); and beta - 13- 30 Hz? These bands are of particular importance because they have been associated with errors, dopamine, and are abnormal in schizophrenia and Parkinson's disease.<br /> b. Power spectra and time-frequency analyses may justify the authors focus. I would show these (y-axis - frequency, x-axis - time, z-axis, power).

(7) PC3 as an autocorrelation doesn't seem the to be right way to infer theta entrainment or spike-field relationships, as PCA can be vulnerable to phantom oscillations, and coherence can be transient. It is also difficult to compare to traditional measures of phase-locking. Why not simply use spike-field coherence? This is particularly important with reference to the human literature, which the authors invoke.

Reviewer #3 (Public Review):

Summary:

The study investigated decision making in rats choosing between small immediate rewards and larger delayed rewards, in a task design where the size of the immediate rewards decreased when this option was chosen and increased when it was not chosen. The authors conceptualise this task as involving two different types of cognitive effort; 'resistance-based' effort putatively needed to resist the smaller immediate reward, and 'resource-based' effort needed to track the changing value of the immediate reward option. They argue based on analyses of the behaviour, and computational modelling, that rats use different strategies in different sessions, with one strategy in which they consistently choose the delayed reward option irrespective of the current immediate reward size, and another strategy in which they preferentially choose the immediate reward option when the immediate reward size is large, and the delayed reward option when the immediate reward size is small. The authors recorded neural activity in anterior cingulate cortex (ACC) and argue that ACC neurons track the value of the immediate reward option irrespective of the strategy the rats are using. They further argue that the strategy the rats are using modulates their estimated value of the immediate reward option, and that oscillatory activity in the 6-12Hz theta band occurs when subjects use the 'resistance-based' strategy of choosing the delayed option irrespective of the current value of the immediate reward option. If solid, these findings will be of interest to researchers working on cognitive control and ACCs involvement in decision making. However, there are some issues with the experiment design, reporting, modelling and analysis which currently preclude high confidence in the validity of the conclusions.

Strengths:

The behavioural task used is interesting and the recording methods should enable the collection of good quality single unit and LFP electrophysiology data. The authors recorded from a sizable sample of subjects for this type of study. The approach of splitting the data into sessions where subjects used different strategies and then examining the neural correlates of each is in principle interesting, though I have some reservations about the strength of evidence for the existence of multiple strategies.

Weaknesses:

The dataset is very unbalanced in terms of both the number of sessions contributed by each subject, and their distribution across the different putative behavioural strategies (see table 1), with some subjects contributing 9 or 10 sessions and others only one session, and it is not clear from the text why this is the case. Further, only 3 subjects contribute any sessions to one of the behavioural strategies, while 7 contribute data to the other such that apparent differences in brain activity between the two strategies could in fact reflect differences between subjects, which could arise due to e.g. differences in electrode placement. To firm up the conclusion that neural activity is different in sessions where different strategies are thought to be employed, it would be important to account for potential cross-subject variation in the data. The current statistical methods don't do this as they all assume fixed effects (e.g. using trials or neurons as the experimental unit and ignoring which subject the neuron/trial came from).

It is not obvious that the differences in behaviour between the sessions characterised as using the 'G1' and 'G2' strategies actually imply the use of different strategies, because the behavioural task was different in these sessions, with a shorter wait (4 seconds vs 8 seconds) for the delayed reward in the G1 strategy sessions where the subjects consistently preferred the delayed reward irrespective of the current immediate reward size. Therefore the differences in behaviour could be driven by difference in the task (i.e. external world) rather than a difference in strategy (internal to the subject). It seems plausible that the higher value of the delayed reward option when the delay is shorter could account for the high probability of choosing this option irrespective of the current value of the immediate reward option, without appealing to the subjects using a different strategy.

Further, even if the differences in behaviour do reflect different behavioural strategies, it is not obvious that these correspond to allocation of different types of cognitive effort. For example, subjects' failure to modify their choice probabilities to track the changing value of the immediate reward option might be due simply to valuing the delayed reward option higher, rather than not allocating cognitive effort to tracking immediate option value (indeed this is suggested by the neural data). Conversely, if the rats assign higher value to the delayed reward option in the G1 sessions, it is not obvious that choosing it requires overcoming 'resistance' through cognitive effort.

The RL modelling used to characterise the subject's behavioural strategies made some unusual and arguably implausible assumptions:

i) The goal of the agent was to maximise the value of the immediate reward option (ival), rather than the standard assumption in RL modelling that the goal is to maximise long-run (e.g. temporally discounted) reward. It is not obvious why the rats should be expected to care about maximising the value of only one of their two choice options rather than distributing their choices to try and maximise long run reward.

ii) The modelling assumed that the subject's choice could occur in 7 different states, defined by the history of their recent choices, such that every successive choice was made in a different state from the previous choice. This is a highly unusual assumption (most modelling of 2AFC tasks assumes all choices occur in the same state), as it causes learning on one trial not to generalise to the next trial, but only to other future trials where the recent choice history is the same.

iii) The value update was non-standard in that rather than using the trial outcome (i.e. the amount of reward obtained) as the update target, it instead appeared to use some function of the value of the immediate reward option (it was not clear to me from the methods exactly how the fival and fqmax terms in the equation are calculated) irrespective of whether the immediate reward option was actually chosen.

iv) The model used an e-greedy decision rule such that the probability of choosing the highest value option did not depend on the magnitude of the value difference between the two options. Typically, behavioural modelling uses a softmax decision rule to capture a graded relationship between choice probability and value difference.

v) Unlike typical RL modelling where the learned value differences drive changes in subjects' choice preferences from trial to trial, to capture sensitivity to the value of the immediately rewarding option the authors had to add in a bias term which depended directly on this value (not mediated by any trial-to-trial learning). It is not clear how the rat is supposed to know the current trial ival if not by learning over previous trials, nor what purpose the learning component of the model serves if not to track the value of the immediate reward option.

Given the task design, a more standard modelling approach would be to treat each choice as occurring in the same state, with the (temporally discounted) value of the outcomes obtained on each trial updating the value of the chosen option, and choice probabilities driven in a graded way (e.g. softmax) by the estimated value difference between the options. It would be useful to explicitly perform model comparison (e.g. using cross-validated log-likelihood with fitted parameters) of the authors proposed model against more standard modelling approaches to test whether their assumptions are justified. It would also be useful to use logistic regression to evaluate how the history of choices and outcomes on recent trials affects the current trial choice, and compare these granular aspects of the choice data with simulated data from the model.

There were also some issues with the analyses of neural data which preclude strong confidence in their conclusions:

Figure 4I makes the striking claim that ACC neurons track the value of the immediately rewarding option equally accurately in sessions where two putative behavioural strategies were used, despite the behaviour being insensitive to this variable in the G1 strategy sessions. The analysis quantifies the strength of correlation between a component of the activity extracted using a decoding analysis and the value of the immediate reward option. However, as far as I could see this analysis was not done in a cross-validated manner (i.e. evaluating the correlation strength on test data that was not used for either training the MCML model or selecting which component to use for the correlation). As such, the chance level correlation will certainly be greater than 0, and it is not clear whether the observed correlations are greater than expected by chance.

An additional caveat with the claim that ACC is tracking the value of the immediate reward option is that this value likely correlates with other behavioural variables, notably the current choice and recent choice history, that may be encoded in ACC. Encoding analyses (e.g. using linear regression to predict neural activity from behavioural variables) could allow quantification of the variance in ACC activity uniquely explained by option values after controlling for possible influence of other variables such as choice history (e.g. using a coefficient of partial determination).

Figure 5 argues that there are systematic differences in how ACC neurons represent the value of the immediate option (ival) in the G1 and G2 strategy sessions. This is interesting if true, but it appears possible that the effect is an artefact of the different distribution of option values between the two session types. Specifically, due to the way that ival is updated based on the subjects' choices, in G1 sessions where the subjects are mostly choosing the delayed option, ival will on average be higher than in G2 sessions where they are choosing the immediate option more often. The relative number of high, medium and low ival trials in the G1 and G2 sessions will therefore be different, which could drive systematic differences in the regression fit in the absence of real differences in the activity-value relationship. I have created an ipython notebook illustrating this, available at: https://notebooksharing.space/view/a3c4504aebe7ad3f075aafaabaf93102f2a28f8c189ab9176d4807cf1565f4e3. To verify that this is not driving the effect it would be important to balance the number of trials at each ival level across sessions (e.g. by subsampling trials) before running the regression.

Author response:

eLife assessment

The authors present a potentially useful approach of broad interest arguing that anterior cingulate cortex (ACC) tracks option values in decisions involving delayed rewards. The authors introduce the idea of a resource-based cognitive effort signal in ACC ensembles and link ACC theta oscillations to a resistance-based strategy. The evidence supporting these new ideas is incomplete and would benefit from additional detail and more rigorous analyses and computational methods.

The reviewers have provided several excellent suggestions and pointed out important shortcomings of our manuscript. We are grateful for their efforts. To address these concerns, we are planning a major revision to the manuscript. In the revision, our goal is to address each of the reviewer’s concerns and codify the evidence for resistance- and resource-based control signals in the rat anterior cingulate cortex. We have provided a nonexhaustive list we plan to address in the point by point responses below.   

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Young (2.5 mo [adolescent]) rats were tasked to either press one lever for immediate reward or another for delayed reward.

Please note that at the time of testing and training that the rats were > 4 months old.

The task had a complex structure in which (1) the number of pellets provided on the immediate reward lever changed as a function of the decisions made, (2) rats were prevented from pressing the same lever three times in a row. Importantly, this task is very different from most intertemporal choice tasks which adjust delay (to the delayed lever), whereas this task held the delay constant and adjusted the number of 20 mg sucrose pellets provided on the immediate value lever.

Several studies parametrically vary the immediate lever (PMID: 39119916, 31654652, 28000083, 26779747, 12270518, 19389183). While most versions of the task will yield qualitatively similar estimates of discounting, the adjusting amount is preferred as it provides the most consistent estimates (PMID: 22445576). More specifically this version of the task avoids contrast effects of that result from changing the delay during the session (PMID: 23963529, 24780379, 19730365, 35661751) which complicates value estimates.

Analyses are based on separating sessions into groups, but group membership includes arbitrary requirements and many sessions have been dropped from the analyses.

We are in discussions about how to address this valid concern. This includes simply splitting the data by delay. This approach, however, has conceptual problems that we will also lay out in a full revision.  

Computational modeling is based on an overly simple reinforcement learning model, as evidenced by fit parameters pegging to the extremes.

We apologize for not doing a better job of explaining the advantages of this type of model for the present purposes. Nevertheless, given the clear lack of enthusiasm, we felt it was better to simply update the model as suggested by the Reviewers. The straightforward modifications have now been implemented and we are currently in discussion about how the new results fit into the larger narrative.

The neural analysis is overly complex and does not contain the necessary statistics to assess the validity of their claims.

We plan to streamline the existing analysis and add statistics, where required, to address this concern.

Strengths:

The task is interesting.

Thank you for the positive comment

Weaknesses:

Behavior:

The basic behavioral results from this task are not presented. For example, "each recording session consisted of 40 choice trials or 45 minutes". What was the distribution of choices over sessions? Did that change between rats? Did that change between delays? Were there any sequence effects? (I recommend looking at reaction times.) Were there any effects of pressing a lever twice vs after a forced trial?

Animals tend to make more immediate choices as the delay is extended, which is reflected in Figure 1. We will add more detail and additional statistics to address these questions. 

This task has a very complicated sequential structure that I think I would be hard pressed to follow if I were performing this task.

Human tasks implement a similar task structure (PMID: 26779747). Please note the response above that outlines the benefits of using of this task.   

Before diving into the complex analyses assuming reinforcement learning paradigms or cognitive control, I would have liked to have understood the basic behaviors the rats were taking. For example, what was the typical rate of lever pressing? If the rats are pressing 40 times in 45 minutes, does waiting 8s make a large difference?

This is a good suggestion. However, rats do not like waiting for rewards, even small delays. Going from the 4 à 8 sec delay results in more immediate choices, indicating that the rats will forgo waiting for a smaller reinforcer at the 8 sec delay as compared to the 4 sec.  

For that matter, the reaction time from lever appearance to lever pressing would be very interesting (and important). Are they making a choice as soon as the levers appear? Are they leaning towards the delay side, but then give in and choose the immediate lever? What are the reaction time hazard distributions?

These are excellent suggestions. We are looking into implementing them.

It is not clear that the animals on this task were actually using cognitive control strategies on this task. One cannot assume from the task that cognitive control is key. The authors only consider a very limited number of potential behaviors (an overly simple RL model). On this task, there are a lot of potential behavioral strategies: "win-stay/lose-shift", "perseveration", "alternation", even "random choices" should be considered.

The strategies the Reviewer mentioned are descriptors of the actual choices the rats made. For example, perseveration means the rat is choosing one of the levers at an excessively high rate whereas alternation means it is choosing the two levers more or less equally, independent of payouts. But the question we are interested in is why? We are arguing that the type of cognitive control determines the choice behavior but cognitive control is an internal variable that guides behavior, rather than simply a descriptor of the behavior. For example, the animal opts to perseverate on the delayed lever because the cognitive control required to track ival is too high. We then searched the neural data for signatures of the two types of cognitive control.

The delay lever was assigned to the "non-preferred side". How did side bias affect the decisions made?

The side bias clearly does not impact performance as the animals prefer the delay lever at shorter delays, which works against this bias.

The analyses based on "group" are unjustified. The authors compare the proportion of delayed to immediate lever press choices on the non-forced trials and then did k-means clustering on this distribution. But the distribution itself was not shown, so it is unclear whether the "groups" were actually different. They used k=3, but do not describe how this arbitrary number was chosen. (Is 3 the optimal number of clusters to describe this distribution?) Moreover, they removed three group 1 sessions with an 8s delay and two group 2 sessions with a 4s delay, making all the group 1 sessions 4s delay sessions and all group 2 sessions 8s delay sessions. They then ignore group 3 completely. These analyses seem arbitrary and unnecessarily complex. I think they need to analyze the data by delay. (How do rats handle 4s delay sessions? How do rats handle 6s delay sessions? How do rats handle 8s delay sessions?). If they decide to analyze the data by strategy, then they should identify specific strategies, model those strategies, and do model comparison to identify the best explanatory strategy. Importantly, the groups were session-based, not rat based, suggesting that rats used different strategies based on the delay to the delayed lever.

These are excellent points and, as stated above, we are in the process revisiting the group assignments in an effort allay these criticisms.

The reinforcement learning model used was overly simple. In particular, the RL model assumes that the subjects understand the task structure, but we know that even humans have trouble following complex task structures. Moreover, we know that rodent decision-making depends on much more complex strategies (model-based decisions, multi-state decisions, rate-based decisions, etc). There are lots of other ways to encode these decision variables, such as softmax with an inverse temperature rather than epsilon-greedy. The RL model was stated as a given and not justified. As one critical example, the RL model fit to the data assumed a constant exponential discounting function, but it is well-established that all animals, including rodents, use hyperbolic discounting in intertemporal choice tasks. Presumably this changes dramatically the effect of 4s and 8s. As evidence that the RL model is incomplete, the parameters found for the two groups were extreme. (Alpha=1 implies no history and only reacting to the most recent event. Epsilon=0.4 in an epsilon-greedy algorithm is a 40% chance of responding randomly.)

Please see our response above. We agree that the approach was not justified, but we do not agree that it is invalid. Simply stated, a softmax approach gives the best fit to the choice behavior, whereas our epsilon-greedy approach attempted to reproduce the choice behavior using a naïve agent that progressively learns the values of the two levers on a choice-by-choice basis. The epsilon-greedy approach can therefore tell us whether it is possible to reproduce the choice behavior by an agent that is only tracking ival. Given our discovery of an ival-tracking signal in ACC, we believed that this was a critical point (although admittedly we did a poor job of communicating it). However, we also appreciate that important insights can be gained by fitting a model to the data as suggested. In fact, we had implemented this approach initially and are currently reconsidering what it can tell us in light of the Reviewers comments.

The authors do add a "dbias" (which is a preference for the delayed lever) term to the RL model, but note that it has to be maximal in the 4s condition to reproduce group 2 behavior, which means they are not doing reinforcement learning anymore, just choosing the delayed lever.

Exactly. The model results indicated that a naïve agent that relied only on ival tracking would not behave in this manner. Hence it therefore was unlikely that the G1 animals were using an ival-tracking strategy, even though a strong ival-tracking signal was present in ACC.

Neurophysiology:

The neurophysiology figures are unclear and mostly uninterpretable; they do not show variability, statistics or conclusive results.

While the reviewer is justified in criticizing the clarity of the figures, the statement that “they do not show variability, statistics or conclusive results” is demonstrably false. Each of the figures presented in the manuscript, except Figure 3, are accompanied by statistics and measures of variability. This comment is hyperbolic and not justified.  

Figure 3 was an attempt to show raw neural data to better demonstrate how robust the ivalue tracking signal is.

As with the behavior, I would have liked to have seen more traditional neurophysiological analyses first. What do the cells respond to? How do the manifolds change aligned to the lever presses? Are those different between lever presses?

We provide several figures describing how neurons change firing rates in response to varying reward. We are unsure what the reviewer means by “traditional analysis”, especially since this is immediately followed by a request for an assessment of neural manifolds. That said, we are developing ways to make the analysis more intuitive and, hopefully, more “traditional”.

Are there changes in cellular information (both at the individual and ensemble level) over time in the session?

We provide several analyses of how firing rate changes over trials in relation to ival over time in the session.

How do cellular responses differ during that delay while both levers are out, but the rats are not choosing the immediate lever?

It is not clear to us how this analysis addresses our hypothesis regarding control signals in ACC.

Figure 3, for example, claims that some of the principal components tracked the number of pellets on the immediate lever ("ival"), but they are just two curves. No statistics, controls, or justification for this is shown. BTW, on Figure 3, what is the event at 200s?

Figure 3 will be folded into one of the other figures that contains the summary statistics.

I'm confused. On Figure 4, the number of trials seems to go up to 50, but in the methods, they say that rats received 40 trials or 45 minutes of experience.

This analysis included force trials. The max of the session is 40 choice trials. We will clarify in the revised manuscript. 

At the end of page 14, the authors state that the strength of the correlation did not differ by group and that this was "predicted" by the RL modeling, but this statement is nonsensical, given that the RL modeling did not fit the data well, depended on extreme values. Moreover, this claim is dependent on "not statistically detectable", which is, of course, not interpretable as "not different".

We plan to revisit this analysis and the RL model.

There is an interesting result on page 16 that the increases in theta power were observed before a delayed lever press but not an immediate lever press, and then that the theta power declined after an immediate lever press.

Thank you for the positive comment.

These data are separated by session group (again group 1 is a subset of the 4s sessions, group 2 is a subset of the 8s sessions, and group 3 is ignored). I would much rather see these data analyzed by delay itself or by some sort of strategy fit across delays.

Provisional analysis indicates that the results hold up over delays, rather than the groupings in the paper. We will address this in a full revision of the manuscript.

That being said, I don't see how this description shows up in Figure 6. What does Figure 6 look like if you just separate the sessions by delay?

We are unclear what the reviewer means by “this description”.

Discussion:

Finally, it is unclear to what extent this task actually gets at the questions originally laid out in the goals and returned to in the discussion. The idea of cognitive effort is interesting, but there is no data presented that this task is cognitive at all. The idea of a resourced cognitive effort and a resistance cognitive effort is interesting, but presumably the way one overcomes resistance is through resource-limited components, so it is unclear that these two cognitive effort strategies are different.

We view the strong evidence for ival tracking presented herein as a potentially critical component of resource based cognitive effort. We hope to clarify how this task engaged cognitive effort more clearly.  

The authors state that "ival-tracking" (neurons and ensembles that presumably track the number of pellets being delivered on the immediate lever - a fancy name for "expectations") "taps into a resourced-based form of cognitive effort", but no evidence is actually provided that keeping track of the expectation of reward on the immediate lever depends on attention or mnemonic resources. They also state that a "dLP-biased strategy" (waiting out the delay) is a "resistance-based form of cognitive effort" but no evidence is made that going to the delayed side takes effort.

There is a well-developed literature that rats and mice do not like waiting for delayed reinforcers. We contend that enduring something you don’t like takes effort.

The authors talk about theta synchrony, but never actually measure theta synchrony, particularly across structures such as amygdala or ventral hippocampus. The authors try to connect this to "the unpleasantness of the delay", but provide no measures of pleasantness or unpleasantness. They have no evidence that waiting out an 8s delay is unpleasant.

We will better clarify how our measure of Theta power relates to synchrony. There is a well-developed literature that rats and mice do not like waiting for delayed reinforcers.

The authors hypothesize that the "ival-tracking signal" (the expectation of number of pellets on the immediate lever) "could simply reflect the emotional or autonomic response". Aside from the fact that no evidence for this is provided, if this were to be true, then, in what sense would any of these signals be related to cognitive control?

This is proposed as an alternative explanation to the ivalue signal. We provide this as a possibility, never a conclusion. We will clarify this in the revised text. 

Reviewer #2 (Public Review):

Summary:

This manuscript explores the neuronal signals that underlie resistance vs resource-based models of cognitive effort. The authors use a delayed discounting task and computational models to explore these ideas. The authors find that the ACC strongly tracks value and time, which is consistent with prior work. Novel contributions include quantification of a resource-based control signal among ACC ensembles, and linking ACC theta oscillations to a resistance-based strategy.

Strengths:

The experiments and analyses are well done and have the potential to generate an elegant explanatory framework for ACC neuronal activity. The inclusion of local-field potential / spike-field analyses is particularly important because these can be measured in humans.

Thank you for the endorsement of our work.

Weaknesses:

I had questions that might help me understand the task and details of neuronal analyses.

(1) The abstract, discussion, and introduction set up an opposition between resource and resistance based forms of cognitive effort. It's clear that the authors find evidence for each (ACC ensembles = resource, theta=resistance?) but I'm not sure where the data fall on this dichotomy.

a. An overall very simple schematic early in the paper (prior to the MCML model? or even the behavior) may help illustrate the main point.

b. In the intro, results, and discussion, it may help to relate each point to this dichotomy.

c. What would resource-based signals look like? What would resistance based signals look like? Is the main point that resistance-based strategies dominate when delays are short, but resource-based strategies dominate when delays are long?

d. I wonder if these strategies can be illustrated? Could these two measures (dLP vs ival tracking) be plotted on separate axes or extremes, and behavior, neuronal data, LFP, and spectral relationships be shown on these axes? I think Figure 2 is working towards this. Could these be shown for each delay length? This way, as the evidence from behavior, model, single neurons, ensembles, and theta is presented, it can be related to this framework, and the reader can organize the findings.

These are excellent suggestions, and we intend to implement each of them, where possible.

(2) The task is not clear to me.

a. I wonder if a task schematic and a flow chart of training would help readers.

Yes, excellent idea, we intend to include this.

b. This task appears to be relatively new. Has it been used before in rats (Oberlin and Grahame is a mouse study)? Some history / context might help orient readers.

Indeed, this task has been used in rats in several prior studies in rats. Please see the following references (PMID: 39119916, 31654652, 28000083, 26779747, 12270518, 19389183).

c. How many total sessions were completed with ascending delays? Was there criteria for surgeries? How many total recording sessions per animal (of the 54?)

Please note that the delay does not change within a session. There was no criteria for surgery. In addition, we will update Table 1 to make the number of recording sessions more clear.

d. How many trials completed per session (40 trials OR 45 minutes)? Where are there errors? These details are important for interpreting Figure 1.

Every animal in this data set completed 40 trials. We will update the task description to clarify this issue. There are no errors in this task, but rather the task is designed to the tendency to make an impulsive choice (smaller reward now). We will provide clarity to this issue in the revision of the manuscript.   

(3) Figure 1 is unclear to me.

a. Delayed vs immediate lever presses are being plotted - but I am not sure what is red, and what is blue. I might suggest plotting each animal.

We will clarify the colors and look into schemes to graph the data set.

b. How many animals and sessions go into each data point?

This information is in Table 1, but this could be clearer, and we will update the manuscript.

c. Table 1 (which might be better referenced in the paper) refers to rats by session. Is it true that some rats (2 and 8) were not analyzed for the bulk of the paper? Some rats appear to switch strategies, and some stay in one strategy. How many neurons come from each rat?

Table 1 is accurate, and we can add the number of neurons from each animal.

d. Task basics - RT, choice, accuracy, video stills - might help readers understand what is going into these plots

e. Does the animal move differently (i.e., RTs) in G1 vs. G2?

We will look into ways to incorporate this information.

(4) I wasn't sure how clustered G1 vs. G2 vs G3 are. To make this argument, the raw data (or some axis of it) might help.

a. This is particularly important because G3 appears to be a mix of G1 and G2, although upon inspection, I'm not sure how different they really are

b. Was there some objective clustering criteria that defined the clusters?

c. Why discuss G3 at all? Can these sessions be removed from analysis?

These are all excellent suggestions and points. We plan to revisit the strategy to assign sessions to groups, which we hope will address each of these points.

(5) The same applies to neuronal analyses in Fig 3 and 4

a. What does a single neuron peri-event raster look like? I would include several of these.

b. What does PC1, 2 and 3 look like for G1, G2, and G3?

c. Certain PCs are selected, but I'm not sure how they were selected - was there a criteria used? How was the correlation between PCA and ival selected? What about PCs that don't correlate with ival?

d. If the authors are using PCA, then scree plots and PETHs might be useful, as well as comparisons to PCs from time-shuffled / randomized data.

We will make several updates to enhance clarity of the neural data analysis, including adding more representative examples. We feel the need to balance the inclusion of representative examples with groups stats given the concerns raised by R1.

(6) I had questions about the spectral analysis

a. Theta has many definitions - why did the authors use 6-12 Hz? Does it come from the hippocampal literature, and is this the best definition of theta?. What about other bands (delta - 1-4 Hz), theta (4-7 Hz); and beta - 13- 30 Hz? These bands are of particular importance because they have been associated with errors, dopamine, and are abnormal in schizophrenia and Parkinson's disease.

This designation comes mainly from the hippocampal and ACC literature in rodents. In addition, this range best captured the peak in the power spectrum in our data. Note that we focus our analysis on theta give the literature regarding theta in the ACC as a correlate of cognitive controls (references in manuscript). We did interrogate other bands as a sanity check and the results were mostly limited to theta. Given the scope of our manuscript and the concerns raised regarding complexity we are concerned that adding frequency analyses beyond theta obfuscates the take home message. However, we think this is worthy, and we will determine if this can be done in a brief, clear, and effective manner.

b. Power spectra and time-frequency analyses may justify the authors focus. I would show these (y-axis - frequency, x-axis - time, z-axis, power).

This is an excellent suggestion that we look forward to incorporating. 

(7) PC3 as an autocorrelation doesn't seem the to be right way to infer theta entrainment or spike-field relationships, as PCA can be vulnerable to phantom oscillations, and coherence can be transient. It is also difficult to compare to traditional measures of phase-locking. Why not simply use spike-field coherence? This is particularly important with reference to the human literature, which the authors invoke.

Excellent suggestion. We will look into the phantom oscillation issue. Note that PCA provided a way to classify neurons that exhibited peaks in the autocorrelation at theta frequencies. While spike-field coherence is a rigorous tool, it addresses a slightly different question (LFP entrainment). Notwithstanding, we plan to address this issue.  

Reviewer #3 (Public Review):

Summary:

The study investigated decision making in rats choosing between small immediate rewards and larger delayed rewards, in a task design where the size of the immediate rewards decreased when this option was chosen and increased when it was not chosen. The authors conceptualise this task as involving two different types of cognitive effort; 'resistance-based' effort putatively needed to resist the smaller immediate reward, and 'resource-based' effort needed to track the changing value of the immediate reward option. They argue based on analyses of the behaviour, and computational modelling, that rats use different strategies in different sessions, with one strategy in which they consistently choose the delayed reward option irrespective of the current immediate reward size, and another strategy in which they preferentially choose the immediate reward option when the immediate reward size is large, and the delayed reward option when the immediate reward size is small. The authors recorded neural activity in anterior cingulate cortex (ACC) and argue that ACC neurons track the value of the immediate reward option irrespective of the strategy the rats are using. They further argue that the strategy the rats are using modulates their estimated value of the immediate reward option, and that oscillatory activity in the 6-12Hz theta band occurs when subjects use the 'resistance-based' strategy of choosing the delayed option irrespective of the current value of the immediate reward option. If solid, these findings will be of interest to researchers working on cognitive control and ACCs involvement in decision making. However, there are some issues with the experiment design, reporting, modelling and analysis which currently preclude high confidence in the validity of the conclusions.

Strengths:

The behavioural task used is interesting and the recording methods should enable the collection of good quality single unit and LFP electrophysiology data. The authors recorded from a sizable sample of subjects for this type of study. The approach of splitting the data into sessions where subjects used different strategies and then examining the neural correlates of each is in principle interesting, though I have some reservations about the strength of evidence for the existence of multiple strategies.

Thank you for the positive comments.

Weaknesses:

The dataset is very unbalanced in terms of both the number of sessions contributed by each subject, and their distribution across the different putative behavioural strategies (see table 1), with some subjects contributing 9 or 10 sessions and others only one session, and it is not clear from the text why this is the case. Further, only 3 subjects contribute any sessions to one of the behavioural strategies, while 7 contribute data to the other such that apparent differences in brain activity between the two strategies could in fact reflect differences between subjects, which could arise due to e.g. differences in electrode placement. To firm up the conclusion that neural activity is different in sessions where different strategies are thought to be employed, it would be important to account for potential cross-subject variation in the data. The current statistical methods don't do this as they all assume fixed effects (e.g. using trials or neurons as the experimental unit and ignoring which subject the neuron/trial came from).

This is an important issue that we plan to address with additional analysis in the manuscript update.

It is not obvious that the differences in behaviour between the sessions characterised as using the 'G1' and 'G2' strategies actually imply the use of different strategies, because the behavioural task was different in these sessions, with a shorter wait (4 seconds vs 8 seconds) for the delayed reward in the G1 strategy sessions where the subjects consistently preferred the delayed reward irrespective of the current immediate reward size. Therefore the differences in behaviour could be driven by difference in the task (i.e. external world) rather than a difference in strategy (internal to the subject). It seems plausible that the higher value of the delayed reward option when the delay is shorter could account for the high probability of choosing this option irrespective of the current value of the immediate reward option, without appealing to the subjects using a different strategy.

Further, even if the differences in behaviour do reflect different behavioural strategies, it is not obvious that these correspond to allocation of different types of cognitive effort. For example, subjects' failure to modify their choice probabilities to track the changing value of the immediate reward option might be due simply to valuing the delayed reward option higher, rather than not allocating cognitive effort to tracking immediate option value (indeed this is suggested by the neural data). Conversely, if the rats assign higher value to the delayed reward option in the G1 sessions, it is not obvious that choosing it requires overcoming 'resistance' through cognitive effort.

The RL modelling used to characterise the subject's behavioural strategies made some unusual and arguably implausible assumptions:

i) The goal of the agent was to maximise the value of the immediate reward option (ival), rather than the standard assumption in RL modelling that the goal is to maximise long-run (e.g. temporally discounted) reward. It is not obvious why the rats should be expected to care about maximising the value of only one of their two choice options rather than distributing their choices to try and maximise long run reward.

ii) The modelling assumed that the subject's choice could occur in 7 different states, defined by the history of their recent choices, such that every successive choice was made in a different state from the previous choice. This is a highly unusual assumption (most modelling of 2AFC tasks assumes all choices occur in the same state), as it causes learning on one trial not to generalise to the next trial, but only to other future trials where the recent choice history is the same.

iii) The value update was non-standard in that rather than using the trial outcome (i.e. the amount of reward obtained) as the update target, it instead appeared to use some function of the value of the immediate reward option (it was not clear to me from the methods exactly how the fival and fqmax terms in the equation are calculated) irrespective of whether the immediate reward option was actually chosen.

iv) The model used an e-greedy decision rule such that the probability of choosing the highest value option did not depend on the magnitude of the value difference between the two options. Typically, behavioural modelling uses a softmax decision rule to capture a graded relationship between choice probability and value difference.

v) Unlike typical RL modelling where the learned value differences drive changes in subjects' choice preferences from trial to trial, to capture sensitivity to the value of the immediately rewarding option the authors had to add in a bias term which depended directly on this value (not mediated by any trial-to-trial learning). It is not clear how the rat is supposed to know the current trial ival if not by learning over previous trials, nor what purpose the learning component of the model serves if not to track the value of the immediate reward option.

Given the task design, a more standard modelling approach would be to treat each choice as occurring in the same state, with the (temporally discounted) value of the outcomes obtained on each trial updating the value of the chosen option, and choice probabilities driven in a graded way (e.g. softmax) by the estimated value difference between the options. It would be useful to explicitly perform model comparison (e.g. using cross-validated log-likelihood with fitted parameters) of the authors proposed model against more standard modelling approaches to test whether their assumptions are justified. It would also be useful to use logistic regression to evaluate how the history of choices and outcomes on recent trials affects the current trial choice, and compare these granular aspects of the choice data with simulated data from the model.

Each of the issues outlined above with the RL model a very important. We are currently re-evaluating the RL modeling approach in light of these comments. Please see comments to R1 regarding the model as they are relevant for this as well.

There were also some issues with the analyses of neural data which preclude strong confidence in their conclusions:

Figure 4I makes the striking claim that ACC neurons track the value of the immediately rewarding option equally accurately in sessions where two putative behavioural strategies were used, despite the behaviour being insensitive to this variable in the G1 strategy sessions. The analysis quantifies the strength of correlation between a component of the activity extracted using a decoding analysis and the value of the immediate reward option. However, as far as I could see this analysis was not done in a cross-validated manner (i.e. evaluating the correlation strength on test data that was not used for either training the MCML model or selecting which component to use for the correlation). As such, the chance level correlation will certainly be greater than 0, and it is not clear whether the observed correlations are greater than expected by chance.

This is an astute observation and we plan to address this concern. We agree that cross-validation may provide an appropriate tool here.

An additional caveat with the claim that ACC is tracking the value of the immediate reward option is that this value likely correlates with other behavioural variables, notably the current choice and recent choice history, that may be encoded in ACC. Encoding analyses (e.g. using linear regression to predict neural activity from behavioural variables) could allow quantification of the variance in ACC activity uniquely explained by option values after controlling for possible influence of other variables such as choice history (e.g. using a coefficient of partial determination).

This is also an excellent point that we plan to address the manuscript update.

Figure 5 argues that there are systematic differences in how ACC neurons represent the value of the immediate option (ival) in the G1 and G2 strategy sessions. This is interesting if true, but it appears possible that the effect is an artefact of the different distribution of option values between the two session types. Specifically, due to the way that ival is updated based on the subjects' choices, in G1 sessions where the subjects are mostly choosing the delayed option, ival will on average be higher than in G2 sessions where they are choosing the immediate option more often. The relative number of high, medium and low ival trials in the G1 and G2 sessions will therefore be different, which could drive systematic differences in the regression fit in the absence of real differences in the activity-value relationship. I have created an ipython notebook illustrating this, available at: https://notebooksharing.space/view/a3c4504aebe7ad3f075aafaabaf93102f2a28f8c189ab9176d4807cf1565f4e3. To verify that this is not driving the effect it would be important to balance the number of trials at each ival level across sessions (e.g. by subsampling trials) before running the regression.

Excellent point and thank you for the notebook. We explored a similar approach previously but did not pursue it to completion. We will re-investigate this issue.

Joint Public Review:

Summary:

This study retrospectively analyzed clinical data to develop a risk prediction model for pulmonary hypertension in high-altitude populations. This finding holds clinical significance as it can be used for intuitive and individualized prediction of pulmonary hypertension risk in these populations. The strength of evidence is high, utilizing a large cohort of 6,603 patients and employing statistical methods such as LASSO regression. The model demonstrates satisfactory performance metrics, including AUC values and calibration curves, enhancing its clinical applicability.

Strengths:

(1) Large Sample Size: The study utilizes a substantial cohort of 6,603 subjects, enhancing the reliability and generalizability of the findings.

(2) Robust Methodology: The use of advanced statistical techniques, including least absolute shrinkage and selection operator (LASSO) regression and multivariate logistic regression, ensures the selection of optimal predictive features.

(3) Clinical Utility: The developed nomograms are user-friendly and can be easily implemented in clinical settings, particularly in resource-limited high-altitude regions.

(4) Performance Metrics: The models demonstrate satisfactory performance, with strong AUC values and well-calibrated curves, indicating accurate predictions.

Weaknesses:

(1) Lack of External Validation: The models were validated internally, but external validation with cohorts from other high-altitude regions is necessary to confirm their generalizability.

(2) Simplistic Predictors: The reliance on ECG and basic demographic data may overlook other potential predictors that could improve the models' accuracy and predictive power.

(3) Regional Specificity: The study's cohort is limited to Tibet, and the findings may not be directly applicable to other high-altitude populations without further validation.

Reviewer #5 (Public Review):

After reading the manuscript and the concerns raised by reviewer 2 I see both sides of the argument - the relative location of trigeminal nucleus versus the inferior olive is quite different in elephants (and different from previous studies in elephants), but when there is a large disproportionate magnification of a behaviorally relevant body part at most levels of the nervous system (certainly in the cortex and thalamus), you can get major shifting in the location of different structures. In the case of the elephant, it looks like there may be a lot of shifting. Something that is compelling is that the number of modules separated but the myelin bands correspond to the number of trunk folds which is different in the different elephants. This sort of modular division based on body parts is a general principle of mammalian brain organization (demonstrated beautifully for the cuneate and gracile nucleus in primates, VP in most of species, S1 in a variety of mammals such as the star nosed mole and duck-billed platypus). I don't think these relative changes in the brainstem would require major genetic programming - although some surely exist. Rodents and elephants have been independently evolving for over 60 million years so there is a substantial amount of time for changes in each l lineage to occur.

I agree that the authors have identified the trigeminal nucleus correctly, although comparisons with more out-groups would be needed to confirm this (although I'm not suggesting that the authors do this). I also think the new figure (which shows previous divisions of the brainstem versus their own) allows the reader to consider these issues for themselves. When reviewing this paper, I actually took the time to go through atlases of other species and even look at some of my own data from highly derived species. Establishing homology across groups based only on relative location is tough especially when there appears to be large shifts in the relative location of structures. My thoughts are that the authors did an extraordinary amount of work on obtaining, processing and analyzing this extremely valuable tissue. They document their work with images of the tissue and their arguments for their divisions are solid. I feel that they have earned the right to speculate - with qualifications - which they provide.

eLife assessment

This valuable study uses neuroanatomical techniques to investigate somatosensory projections from the elephant trunk to the brainstem. Given its unique specializations, understanding how the elephant trunk is represented within the brain is of general interest to evolutionary and comparative neuroscientists. The authors present solid evidence for the existence of a novel isomorphism in which the folds of the trunk are mapped onto the trigeminal nucleus; however, due to their unusual structure, some uncertainty remains about the identification and anatomical organization of nuclei within the elephant brainstem.

Reviewer #1 (Public Review):

This manuscript remains an intriguing investigation of the elephant brainstem, with particular attention drawn to possible sensory and motor representation of the renowned trunk of African and Asian elephants. As the authors note, this area has traditionally been identified as part of the superior olivary complex and associated with the fine motor control of the trunk; however, notable patterns within myelin stripes suggest that its parcellation may relate to specific regions/folds found along the long axis of the trunk, including elaborated regions for the trunk "finger" distal end.

In this iteration of the manuscript, the researchers have provided peripherin antibody staining within the regions they have identified as the trigeminal nucleus and the superior olive. These data, with abundant peripherin expression within climbing fibers of the presumed superior olive and relatively lower expression within the trigeminal nucleus, bolster their interpretation of having comprehensively identified the trigeminal nucleus and trunk representation via a battery of neuroanatomical methods.

All other conclusions remain the same, and these data have provoked intriguing and animated discussion on classification of neuroanatomical structure, particularly in species with relatively limited access to specimens. Most significantly, these discussions have underscored the fundamental nature of comparative methods (from protein to cellular to anatomical levels), including interpreting homologous structures among species of varying levels of relatedness.

Reviewer #2 (Public Review):

Here I submit my previous review and a great deal of additional information following on from the initial review and the response by the authors.

* Initial Review *

Assessment:

This manuscript is based upon the unprecedented identification of an apparently highly unusual trigeminal nuclear organization within the elephant brainstem, related to a large trigeminal nerve in these animals. The apparently highly specialized elephant trigeminal nuclear complex identified in the current study has been classified as the inferior olivary nuclear complex in four previous studies of the elephant brainstem. The entire study is predicated upon the correct identification of the trigeminal sensory nuclear complex and the inferior olivary nuclear complex in the elephant, and if this is incorrect, then the remainder of the manuscript is merely unsupported speculation. There are many reasons indicating that the trigeminal nuclear complex is misidentified in the current study, rendering the entire study, and associated speculation, inadequate at best, and damaging in terms of understanding elephant brains and behaviour at worst.

Original Public Review:

The authors describe what they assert to be a very unusual trigeminal nuclear complex in the brainstem of elephants, and based on this, follow with many speculations about how the trigeminal nuclear complex, as identified by them, might be organized in terms of the sensory capacity of the elephant trunk.<br /> The identification of the trigeminal nuclear complex/inferior olivary nuclear complex in the elephant brainstem is the central pillar of this manuscript from which everything else follows, and if this is incorrect, then the entire manuscript fails, and all the associated speculations become completely unsupported.

The authors note that what they identify as the trigeminal nuclear complex has been identified as the inferior olivary nuclear complex by other authors, citing Shoshani et al. (2006; 10.1016/j.brainresbull.2006.03.016) and Maseko et al (2013; 10.1159/000352004), but fail to cite either Verhaart and Kramer (1958; PMID 13841799) or Verhaart (1962; 10.1515/9783112519882-001). These four studies are in agreement, but the current study differs.

Let's assume for the moment that the four previous studies are all incorrect and the current study is correct. This would mean that the entire architecture and organization of the elephant brainstem is significantly rearranged in comparison to ALL other mammals, including humans, previously studied (e.g. Kappers et al. 1965, The Comparative Anatomy of the Nervous System of Vertebrates, Including Man, Volume 1 pp. 668-695) and the closely related manatee (10.1002/ar.20573). This rearrangement necessitates that the trigeminal nuclei would have had to "migrate" and shorten rostrocaudally, specifically and only, from the lateral aspect of the brainstem where these nuclei extend from the pons through to the cervical spinal cord (e.g. the Paxinos and Watson rat brain atlases), the to the spatially restricted ventromedial region of specifically and only the rostral medulla oblongata. According to the current paper the inferior olivary complex of the elephant is very small and located lateral to their trigeminal nuclear complex, and the region from where the trigeminal nuclei are located by others appears to be just "lateral nuclei" with no suggestion of what might be there instead.

Such an extraordinary rearrangement of brainstem nuclei would require a major transformation in the manner in which the mutations, patterning, and expression of genes and associated molecules during development occur. Such a major change is likely to lead to lethal phenotypes, making such a transformation extremely unlikely. Variations in mammalian brainstem anatomy are most commonly associated with quantitative changes rather than qualitative changes (10.1016/B978-0-12-804042-3.00045-2).

The impetus for the identification of the unusual brainstem trigeminal nuclei in the current study rests upon a previous study from the same laboratory (10.1016/j.cub.2021.12.051) that estimated that the number of axons contained in the infraorbital branch of the trigeminal nerve that innervate the sensory surfaces of the trunk is approximately 400 000. Is this number unusual? In a much smaller mammal with a highly specialized trigeminal system, the platypus, the number of axons innervating the sensory surface of the platypus bill skin comes to 1 344 000 (10.1159/000113185). Yet, there is no complex rearrangement of the brainstem trigeminal nuclei in the brain of the developing or adult platypus (Ashwell, 2013, Neurobiology of Monotremes), despite the brainstem trigeminal nuclei being very large in the platypus (10.1159/000067195). Even in other large-brained mammals, such as large whales that do not have a trunk, the number of axons in the trigeminal nerve ranges between 400,000 and 500,000 (10.1007/978-3-319-47829-6_988-1). The lack of comparative support for the argument forwarded in the previous and current study from this laboratory, and that the comparative data indicates that the brainstem nuclei do not change in the manner suggested in the elephant, argues against the identification of the trigeminal nuclei as outlined in the current study. Moreover, the comparative studies undermine the prior claim of the authors, informing the current study, that "the elephant trigeminal ganglion ... point to a high degree of tactile specialization in elephants" (10.1016/j.cub.2021.12.051). While clearly the elephant has tactile sensitivity in the trunk, it is questionable as to whether what has been observed in elephants is indeed "truly extraordinary".

But let's look more specifically at the justification outlined in the current study to support their identification of the unusually located trigeminal sensory nuclei of the brainstem.

(1) Intense cytochrome oxidase reactivity<br /> (2) Large size of the putative trunk module<br /> (3) Elongation of the putative trunk module<br /> (4) Arrangement of these putative modules correspond to elephant head anatomy<br /> (5) Myelin stripes within the putative trunk module that apparently match trunk folds<br /> (6) Location apparently matches other mammals<br /> (7) Repetitive modular organization apparently similar to other mammals.<br /> (8) The inferior olive described by other authors lacks the lamellated appearance of this structure in other mammals

Let's examine these justifications more closely.

(1) Cytochrome oxidase histochemistry is typically used as an indicative marker of neuronal energy metabolism. The authors indicate, based on the "truly extraordinary" somatosensory capacities of the elephant trunk, that any nuclei processing this tactile information should be highly metabolically active, and thus should react intensely when stained for cytochrome oxidase. We are told in the methods section that the protocols used are described by Purkart et al (2022) and Kaufmann et al (2022). In neither of these cited papers is there any description, nor mention, of the cytochrome oxidase histochemistry methodology, thus we have no idea of how this histochemical staining was done. In order to obtain the best results for cytochrome oxidase histochemistry, the tissue is either processed very rapidly after buffer perfusion to remove blood or in recently perfusion-fixed tissue (e.g., 10.1016/0165-0270(93)90122-8). Given: (1) the presumably long post-mortem interval between death and fixation - "it often takes days to dissect elephants"; (2) subsequent fixation of the brains in 4% paraformaldehyde for "several weeks"; (3) The intense cytochrome oxidase reactivity in the inferior olivary complex of the laboratory rat (Gonzalez-Lima, 1998, Cytochrome oxidase in neuronal metabolism and Alzheimer's diseases); and (4) The lack of any comparative images from other stained portions of the elephant brainstem; it is difficult to support the justification as forwarded by the authors. It is likely that the histochemical staining observed is background reactivity from the use of diaminobenzidine in the staining protocol. Thus, this first justification is unsupported.<br /> Justifications (2), (3), and (4) are sequelae from justification (1). In this sense, they do not count as justifications, but rather unsupported extensions.

(4) and (5) These are interesting justifications, as the paper has clear internal contradictions, and (5) is a sequelae of (4). The reader is led to the concept that the myelin tracts divide the nuclei into sub-modules that match the folding of the skin on the elephant trunk. One would then readily presume that these myelin tracts are in the incoming sensory axons from the trigeminal nerve. However, the authors note that this is not the case: "Our observations on trunk module myelin stripes are at odds with this view of myelin. Specifically, myelin stripes show no tapering (which we would expect if axons divert off into the tissue). More than that, there is no correlation between myelin stripe thickness (which presumably correlates with axon numbers) and trigeminal module neuron numbers. Thus, there are numerous myelinated axons, where we observe few or no trigeminal neurons. These observations are incompatible with the idea that myelin stripes form an axonal 'supply' system or that their prime function is to connect neurons. What do myelin stripe axons do, if they do not connect neurons? We suggest that myelin stripes serve to separate rather than connect neurons." So, we are left with the observation that the myelin stripes do not pass afferent trigeminal sensory information from the "truly extraordinary" trunk skin somatic sensory system, and rather function as units that separate neurons - but to what end? It appears that the myelin stripes are more likely to be efferent axonal bundles leaving the nuclei (to form the olivocerebellar tract). This justification is unsupported.

(6) The authors indicate that the location of these nuclei matches that of the trigeminal nuclei in other mammals. This is not supported in any way. In ALL other mammals in which the trigeminal nuclei of the brainstem have been reported they are found in the lateral aspect of the brainstem, bordered laterally by the spinal trigeminal tract. This is most readily seen and accessible in the Paxinos and Watson rat brain atlases. The authors indicate that the trigeminal nuclei are medial to the facial nerve nucleus, but in every other species, the trigeminal sensory nuclei are found lateral to the facial nerve nucleus. This is most salient when examining a close relative, the manatee (10.1002/ar.20573), where the location of the inferior olive and the trigeminal nuclei matches that described by Maseko et al (2013) for the African elephant. This justification is not supported.

(7) The dual to quadruple repetition of rostro-caudal modules within the putative trigeminal nucleus as identified by the authors relies on the fact that in the neurotypical mammal, there are several trigeminal sensory nuclei arranged in a column running from the pons to the cervical spinal cord, these include (nomenclature from Paxinos and Watson in roughly rostral to caudal order) the Pr5VL, Pr5DM, Sp5O, Sp5I, and Sp5C. But, these nuclei are all located far from the midline and lateral to the facial nerve nucleus, unlike what the authors describe in the elephants. These rostrocaudal modules are expanded upon in Figure 2, and it is apparent from what is shown that the authors are attributing other brainstem nuclei to the putative trigeminal nuclei to confirm their conclusion. For example, what they identify as the inferior olive in figure 2D is likely the lateral reticular nucleus as identified by Maseko et al (2013). This justification is not supported.

(8) In primates and related species, there is a distinct banded appearance of the inferior olive, but what has been termed the inferior olive in the elephant by other authors does not have this appearance, rather, and specifically, the largest nuclear mass in the region (termed the principal nucleus of the inferior olive by Maseko et al, 2013, but Pr5, the principal trigeminal nucleus in the current paper) overshadows the partial banded appearance of the remaining nuclei in the region (but also drawn by the authors of the current paper). Thus, what is at debate here is whether the principal nucleus of the inferior olive can take on a nuclear shape rather than evince a banded appearance. The authors of this paper use this variance as justification that this cluster of nuclei could not possibly be the inferior olive. Such a "semi-nuclear/banded" arrangement of the inferior olive is seen in, for example, giraffe (10.1016/j.jchemneu.2007.05.003), domestic dog, polar bear, and most specifically the manatee (a close relative of the elephant) (brainmuseum.org; 10.1002/ar.20573). This justification is not supported.

Thus, all the justifications forwarded by the authors are unsupported. Based on methodological concerns, prior comparative mammalian neuroanatomy, and prior studies in the elephant and closely related species, the authors fail to support their notion that what was previously termed the inferior olive in the elephant is actually the trigeminal sensory nuclei. Given this failure, the justifications provided above that are sequelae also fail. In this sense, the entire manuscript and all the sequelae are not supported.

What the authors have not done is to trace the pathway of the large trigeminal nerve in the elephant brainstem, as was done by Maseko et al (2013), which clearly shows the internal pathways of this nerve, from the branch that leads to the fifth mesencephalic nucleus adjacent to the periventricular grey matter, through to the spinal trigeminal tract that extends from the pons to the spinal cord in a manner very similar to all other mammals. Nor have they shown how the supposed trigeminal information reaches the putative trigeminal nuclei in the ventromedial rostral medulla oblongata. These are but two examples of many specific lines of evidence that would be required to support their conclusions. Clearly tract tracing methods, such as cholera toxin tracing of peripheral nerves cannot be done in elephants, thus the neuroanatomy must be done properly and with attention to detail to support the major changes indicated by the authors.

So what are these "bumps" in the elephant brainstem?

Four previous authors indicate that these bumps are the inferior olivary nuclear complex. Can this be supported?

The inferior olivary nuclear complex acts "as a relay station between the spinal cord (n.b. trigeminal input does reach the spinal cord via the spinal trigeminal tract) and the cerebellum, integrating motor and sensory information to provide feedback and training to cerebellar neurons" (https://www.ncbi.nlm.nih.gov/books/NBK542242/). The inferior olivary nuclear complex is located dorsal and medial to the pyramidal tracts (which were not labelled in the current study by the authors but are clearly present in Fig. 1C and 2A) in the ventromedial aspect of the rostral medulla oblongata. This is precisely where previous authors have identified the inferior olivary nuclear complex and what the current authors assign to their putative trigeminal nuclei. The neurons of the inferior olivary nuclei project, via the olivocerebellar tract to the cerebellum to terminate in the climbing fibres of the cerebellar cortex.

Elephants have the largest (relative and absolute) cerebellum of all mammals (10.1002/ar.22425), this cerebellum contains 257 x109 neurons (10.3389/fnana.2014.00046; three times more than the entire human brain, 10.3389/neuro.09.031.2009). Each of these neurons appears to be more structurally complex than the homologous neurons in other mammals (10.1159/000345565; 10.1007/s00429-010-0288-3). In the African elephant, the neurons of the inferior olivary nuclear complex are described by Maseko et al (2013) as being both calbindin and calretinin immunoreactive. Climbing fibres in the cerebellar cortex of the African elephant are clearly calretinin immunopositive and also are likely to contain calbindin (10.1159/000345565). Given this, would it be surprising that the inferior olivary nuclear complex of the elephant is enlarged enough to create a very distinct bump in exactly the same place where these nuclei are identified in other mammals?

What about the myelin stripes? These are most likely to be the origin of the olivocerebellar tract and probably only have a coincidental relationship to the trunk. Thus, given what we know, the inferior olivary nuclear complex as described in other studies, and the putative trigeminal nuclear complex as described in the current study, is the elephant inferior olivary nuclear complex. It is not what the authors believe it to be, and they do not provide any evidence that discounts the previous studies. The authors are quite simply put, wrong. All the speculations that flow from this major neuroanatomical error are therefore science fiction rather than useful additions to the scientific literature.

What do the authors actually have?<br /> The authors have interesting data, based on their Golgi staining and analysis, of the inferior olivary nuclear complex in the elephant.

* Review of Revised Manuscript *

Assessment:

There is a clear dichotomy between the authors and this reviewer regarding the identification of specific structures, namely the inferior olivary nuclear complex and the trigeminal nuclear complex, in the brainstem of the elephant. The authors maintain the position that in the elephant alone, irrespective of all the published data on other mammals and previously published data on the elephant brainstem, these two nuclear complexes are switched in location. The authors maintain that their interpretation is correct, but this reviewer maintains that this interpretation is erroneous. The authors expressed concern that the remainder of the paper was not addressed by the reviewer, but the reviewer maintains that these sequelae to the misidentification of nuclear complexes in the elephant brainstem render any of these speculations irrelevant as the critical structures are incorrectly identified. It is this reviewer's opinion that this paper is incorrect. I provide a lot of detail below in order to provide support to the opinion I express.

Public Review of Current Submission:

As indicated in my previous review of this manuscript (see above), it is my opinion that the authors have misidentified, and indeed switched, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex (Vsens). It is this specific point only that I will address in this second review, as this is the crucial aspect of this paper - if the identification of these nuclear complexes in the elephant brainstem by the authors is incorrect, the remainder of the paper does not have any scientific validity.

The authors, in their response to my initial review, claim that I "bend" the comparative evidence against them. They further claim that as all other mammalian species exhibit a "serrated" appearance of the inferior olive, and as the elephant does not exhibit this appearance, what was previously identified as the inferior olive is actually the trigeminal nucleus and vice versa.

For convenience, I will refer to IOM and VsensM as the identification of these structures according to Maseko et al (2013) and other authors and will use IOR and VsensR to refer to the identification forwarded in the study under review.<br /> The IOM/VsensR certainly does not have a serrated appearance in elephants. Indeed, from the plates supplied by the authors in response (Referee Fig. 2), the cytochrome oxidase image supplied and the image from Maseko et al (2013) shows a very similar appearance. There is no doubt that the authors are identifying structures that closely correspond to those provided by Maseko et al (2013). It is solely a contrast in what these nuclear complexes are called and the functional sequelae of the identification of these complexes (are they related to the trunk sensation or movement controlled by the cerebellum?) that is under debate.

Elephants are part of the Afrotheria, thus the most relevant comparative data to resolve this issue will be the identification of these nuclei in other Afrotherian species. Below I provide images of these nuclear complexes, labelled in the standard nomenclature, across several Afrotherian species.

(A) Lesser hedgehog tenrec (Echinops telfairi)

Tenrecs brains are the most intensively studied of the Afrotherian brains, these extensive neuroanatomical studies were undertaken primarily by Heinz Künzle. Below I append images (coronal sections stained with cresol violet) of the IO and Vsens (labelled in the standard mammalian manner) in the lesser hedgehog tenrec. It should be clear that the inferior olive is located in the ventral midline of the rostral medulla oblongata (just like the rat) and that this nucleus is not distinctly serrated. The Vsens is located in the lateral aspect of the medulla skirted laterally by the spinal trigeminal tract (Sp5). These images and the labels indicating structures correlate precisely with that provided by Künzle (1997, 10.1016/S0168- 0102(97)00034-5), see his Figure 1K,L. Thus, in the first case of a related species, there is no serrated appearance of the inferior olive, the location of the inferior olive is confirmed through connectivity with the superior colliculus (a standard connection in mammals) by Künzle (1997), and the location of Vsens is what is considered to be typical for mammals. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Peer Review Image 1.

(B) Giant otter shrew (Potomogale velox)

The otter shrews are close relatives of the Tenrecs. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see hints of the serration of the IO as defined by the authors, but we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Peer Response Image 2.

(C) Four-toed sengi (Petrodromus tetradactylus)

The sengis are close relatives of the Tenrecs and otter shrews, these three groups being part of the Afroinsectiphilia, a distinct branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see vague hints of the serration of the IO (as defined by the authors), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Peer Response Image 3.

(D) Rock hyrax (Procavia capensis)

The hyraxes, along with the sirens and elephants form the Paenungulata branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per the standard mammalian anatomy. Here we see hints of the serration of the IO (as defined by the authors), but we also see evidence of a more "bulbous" appearance of subnuclei of the IO (particularly the principal nucleus), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Peer Review Image 4.

(E) West Indian manatee (Trichechus manatus)

The sirens are the closest extant relatives of the elephants in the Afrotheria. Below I append images of cresyl violet (top) and myelin (bottom) stained coronal sections (taken from the University of Wisconsin-Madison Brain Collection, https://brainmuseum.org, and while quite low in magnification they do reveal the structures under debate) through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see the serration of the IO (as defined by the authors). Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Peer Review Image 5.

These comparisons and the structural identification, with which the authors agree as they only distinguish the elephants from the other Afrotheria, demonstrate that the appearance of the IO can be quite variable across mammalian species, including those with a close phylogenetic affinity to the elephants. Not all mammal species possess a "serrated" appearance of the IO. Thus, it is more than just theoretically possible that the IO of the elephant appears as described prior to this study.

So what about elephants? Below I append a series of images from coronal sections through the African elephant brainstem stained for Nissl, myelin, and immunostained for calretinin. These sections are labelled according to standard mammalian nomenclature. In these complete sections of the elephant brainstem, we do not see a serrated appearance of the IOM (as described previously and in the current study by the authors). Rather the principal nucleus of the IOM appears to be bulbous in nature. In the current study, no image of myelin staining in the IOM/VsensR is provided by the authors. However, in the images I provide, we do see the reported myelin stripes in all stains - agreement between the authors and reviewer on this point. The higher magnification image to the bottom left of the plate shows one of the IOM/VsensR myelin stripes immunostained for calretinin, and within the myelin stripes axons immunopositive for calretinin are seen (labelled with an arrow). The climbing fibres of the elephant cerebellar cortex are similarly calretinin immunopositive (10.1159/000345565). In contrast, although not shown at high magnification, the fibres forming the Sp5 in the elephant (in the Maseko description, unnamed in the description of the authors) show no immunoreactivity to calretinin.

Peer Review Image 6.

Peripherin Immunostaining

In their revised manuscript the authors present immunostaining of peripherin in the elephant brainstem. This is an important addition (although it does replace the only staining of myelin provided by the authors which is unusual as the word myelin is in the title of the paper) as peripherin is known to specifically label peripheral nerves. In addition, as pointed out by the authors, peripherin also immunostains climbing fibres (Errante et al., 1998). The understanding of this staining is important in determining the identification of the IO and Vsens in the elephant, although it is not ideal for this task as there is some ambiguity. Errante and colleagues (1998; Fig. 1) show that climbing fibres are peripherin-immunopositive in the rat. But what the authors do not evaluate is the extensive peripherin staining in the rat Sp5 in the same paper (Errante et al, 1998, Fig. 2). The image provided by the authors of their peripherin immunostaining (their new Figure 2) shows what I would call the Sp5 of the elephant to be strongly peripherin immunoreactive, just like the rat shown in Errant et al (1998), and moreover in the precise position of the rat Sp5! This makes sense as this is where the axons subserving the "extraordinary" tactile sensitivity of the elephant trunk would be found (in the standard model of mammalian brainstem anatomy). Interestingly, the peripherin immunostaining in the elephant is clearly lamellated...this coincides precisely with the description of the trigeminal sensory nuclei in the elephant by Maskeo et al (2013) as pointed out by the authors in their rebuttal. Errante et al (1998) also point out peripherin immunostaining in the inferior olive, but according to the authors this is only "weakly present" in the elephant IOM/VsensR. This latter point is crucial. Surely if the elephant has an extraordinary sensory innervation from the trunk, with 400,000 axons entering the brain, the VsensR/IOM should be highly peripherin-immunopositive, including the myelinated axon bundles?! In this sense, the authors argue against their own interpretation - either the elephant trunk is not a highly sensitive tactile organ, or the VsensR is not the trigeminal nuclei it is supposed to be.

Summary:

(1) Comparative data of species closely related to elephants (Afrotherians) demonstrates that not all mammals exhibit the "serrated" appearance of the principal nucleus of the inferior olive.

(2) The location of the IO and Vsens as reported in the current study (IOR and VsensR) would require a significant, and unprecedented, rearrangement of the brainstem in the elephants independently. I argue that the underlying molecular and genetic changes required to achieve this would be so extreme that it would lead to lethal phenotypes. Arguing that the "switcheroo" of the IO and Vsens does occur in the elephant (and no other mammals) and thus doesn't lead to lethal phenotypes is a circular argument that cannot be substantiated.

(3) Myelin stripes in the subnuclei of the inferior olivary nuclear complex are seen across all related mammals as shown above. Thus, the observation made in the elephant by the authors in what they call the VsensR, is similar to that seen in the IO of related mammals, especially when the IO takes on a more bulbous appearance. These myelin stripes are the origin of the olivocerebellar pathway and are indeed calretinin immunopositive in the elephant as I show.

(4) What the authors see aligns perfectly with what has been described previously, the only difference being the names that nuclear complexes are being called. But identifying these nuclei is important, as any functional sequelae, as extensively discussed by the authors, is entirely dependent upon accurately identifying these nuclei.

(4) The peripherin immunostaining scores an own goal - if peripherin is marking peripheral nerves (as the authors and I believe it is), then why is the VsensR/IOM only "weakly positive" for this stain? This either means that the "extraordinary" tactile sensitivity of the elephant trunk is non-existent, or that the authors have misinterpreted this staining. That there is extensive staining in the fibre pathway dorsal and lateral to the IOR (which I call the spinal trigeminal tract), supports the idea that the authors have misinterpreted their peripherin immunostaining.

(5) Evolutionary expediency. The authors argue that what they report is an expedient way in which to modify the organisation of the brainstem in the elephant to accommodate the "extraordinary" tactile sensitivity. I disagree. As pointed out in my first review, the elephant cerebellum is very large and comprised of huge numbers of morphologically complex neurons. The inferior olivary nuclei in all mammals studied in detail to date, give rise to the climbing fibres that terminate on the Purkinje cells of the cerebellar cortex. It is more parsimonious to argue that, in alignment with the expansion of the elephant cerebellum (for motor control of the trunk), the inferior olivary nuclei (specifically the principal nucleus) have had additional neurons added to accommodate this cerebellar expansion. Such an addition of neurons to the principal nucleus of the inferior olive could readily lead to the loss of the serrated appearance of the principal nucleus of the inferior olive and would require far less modifications in the developmental genetic program that forms these nuclei. This type of quantitative change appears to be the primary way in which structures are altered in the mammalian brainstem.

Reviewer #3 (Public Review):

Summary:

The study claims to investigate trunk representations in elephant trigeminal nuclei located in the brainstem. The researchers identify large protrusions visible from the ventral surface of the brainstem, which they examined using a range of histological methods. However, this ventral location is usually where the inferior olivary complex is found, which challenges the author's assertions about the nucleus under analysis. They find that this brainstem nucleus of elephants contains repeating modules, with a focus on the anterior and largest unit which they define as the putative nucleus principalis trunk module of the trigeminal. The nucleus exhibits low neuron density, with glia outnumbering neurons significantly. The study also utilizes synchrotron X-ray phase contrast tomography to suggest that myelin-stripe-axons traverse this module. The analysis maps myelin-rich stripes in several specimens and concludes that based on their number and patterning they likely correspond with trunk folds; however this conclusion is not well supported if the nucleus has been misidentified.

Strengths:

The strength of this research lies in its comprehensive use of various anatomical methods, including Nissl staining, myelin staining, Golgi staining, cytochrome oxidase labeling, and synchrotron X-ray phase contrast tomography. The inclusion of quantitative data on cell numbers and sizes, dendritic orientation and morphology, and blood vessel density across the nucleus adds a quantitative dimension. Furthermore, the research is commendable for its high-quality and abundant images and figures, effectively illustrating the anatomy under investigation.

Weaknesses:

While the research provides potentially valuable insights if revised to focus on the structure that appears to be an inferior olivary nucleus, there are certain additional weaknesses that warrant further consideration. First, the suggestion that myelin stripes solely serve to separate sensory or motor modules rather than functioning as an "axonal supply system" lacks substantial support due to the absence of information about the neuronal origins and the termination targets of the axons. Postmortem fixed brain tissue limits the ability to trace full axon projections. While the study acknowledges these limitations, it is important to exercise caution in drawing conclusions about the precise role of myelin stripes without a more comprehensive understanding of their neural connections.

Second, the quantification presented in the study lacks comparison to other species or other relevant variables within the elephant specimens (i.e., whole brain or brainstem volume). The absence of comparative data to different species limits the ability to fully evaluate the significance of the findings. Comparative analyses could provide a broader context for understanding whether the observed features are unique to elephants or more common across species. This limitation in comparative data hinders a more comprehensive assessment of the implications of the research within the broader field of neuroanatomy. Furthermore, the quantitative comparisons between African and Asian elephant specimens should include some measure of overall brain size as a covariate in the analyses. Addressing these weaknesses would enable a richer interpretation of the study's findings.

Reviewer #4 (Public Review):

Summary:

The authors report a novel isomorphism in which the folds of the elephant trunk are recognizably mapped onto the principal sensory trigeminal nucleus in the brainstem. Further, they identify the enlarged nucleus as being situated in this species in an unusual ventral midline position.

Strengths:

The identity of the purported trigeminal nucleus and the isomorphic mapping with the trunk folds is supported by multiple lines of evidence: enhanced staining for cytochrome oxidase, an enzyme associated with high metabolic activity; dense vascularization, consistent with high metabolic activity; prominent myelinated bundles that partition the nucleus in a 1:1 mapping of the cutaneous folds in the trunk periphery; near absence of labeling for the anti-peripherin antibody, specific for climbing fibers, which can be seen as expected in the inferior olive; and a high density of glia.

Weaknesses:

Despite the supporting evidence listed above, the identification of the gross anatomical bumps, conspicuous in the ventral midline, is problematic. This would be the standard location of the inferior olive, with the principal trigeminal nucleus occupying a more dorsal position. This presents an apparent contradiction which at a minimum needs further discussion. Major species-specific specializations and positional shifts are well-documented for cortical areas, but nuclear layouts in the brainstem have been considered as less malleable.

Author Response:

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

We carefully read through the second-round reviews and the additional reviews. To us, the review process is somewhat unusual and very much dominated by referee 2, who aggressively insists that we mixed up the trigeminal nucleus and inferior olive and that as a consequence our results are meaningless. We think the stance of referee 2 and the focus on one single issue (the alleged mix-up of trigeminal nucleus and inferior olive) is somewhat unfortunate, leaves out much of our findings and we debated at length on how to deal with further revisions. In the end, we decided to again give priority to addressing the criticism of referees 2, because it is hard to go on with a heavily attacked paper without resolving the matter at stake. The following is a summary of, what we did:

Additional experimental work:

(1) We checked if the peripherin-antibody indeed reliably identifies climbing fibers.

To this end, we sectioned the elephant cerebellum and stained sections with the peripherin-antibody. We find: (i) the cerebellar white matter is strongly reactive for peripherin-antibodies, (ii) cerebellar peripherin-antibody staining of has an axonal appearance. (iii) Cerebellar Purkinje cell somata appear to be ensheated by peripherin-antibody staining. (iv) We observed that the peripherin-antibody reactivity gradually decreases from Purkinje cell somata to the pia in the cerebellar molecular layer. This work is shown in our revised Figure 2. All these four features align with the distribution of climbing fibers (which arrive through the white matter, are axons, ensheat Purkinje cell somata, and innervate Purkinje cell proximally not reaching the pia). In line with previous work, which showed similar cerebellar staining patterns in several species (Errante et al. 1998), we conclude that elephant climbing fibers are strongly reactive for peripherin-antibodies.

(2) We delineated the elephant olivo-cerebellar tract.

The strong peripherin-antibody reactivity of elephant climbing fibers enabled us to delineate the elephant olivo-cerebellar tract. We find the elephant olivo-cerebellar tract is a strongly peripherin-antibody reactive, well-delineated fiber tract several millimeters wide and about a centimeter in height. The unstained olivo-cerebellar tract has a greyish appearance. In the anterior regions of the olivo-cerebellar tract, we find that peripherin-antibody reactive fibers run in the dorsolateral brainstem and approach the cerebellar peduncle, where the tract gradually diminishes in size, presumably because climbing fibers discharge into the peduncle. Indeed, peripherin-antibody reactive fibers can be seen entering the cerebellar peduncle. Towards the posterior end of the peduncle, the olivo-cerebellar disappears (in the dorsal brainstem directly below the peduncle. We note that the olivo-cerebellar tract was referred to as the spinal trigeminal tract by Maseko et al. 2013. We think the tract in question cannot be the spinal trigeminal tract for two reasons: (i) This tract is the sole brainstem source of peripherin-positive climbing fibers entering the peduncle/ the cerebellum; this is the defining characteristic of the olivo-cerebellar tract. (ii) The tract in question is much smaller than the trigeminal nerve, disappears posterior to where the trigeminal nerve enters the brainstem (see below), and has no continuity with the trigeminal nerve; the continuity with the trigeminal nerve is the defining characteristic of the spinal trigeminal tract, however.

The anterior regions of the elephant olivo-cerebellar tract are similar to the anterior regions of olivo-cerebellar tract of other mammals in its dorsolateral position and the relation to the cerebellar peduncle. In its more posterior parts, the elephant olivo-cerebellar tract continues for a long distance (~1.5 cm) in roughly the same dorsolateral position and enters the serrated nucleus that we previously identified as the elephant inferior olive. The more posterior parts of the elephant olivo-cerebellar tract therefore differ from the more posterior parts of the olivo-cerebellar tract of other mammals, which follows a ventromedial trajectory towards a ventromedially situated inferior olive. The implication of our delineation of the elephant olivo-cerebellar tract is that we correctly identified the elephant inferior olive.

(3) An in-depth analysis of peripherin-antibody reactivity also indicates that the trigeminal nucleus receives no climbing fiber input.

We also studied the peripherin-antibody reactivity in and around the trigeminal nucleus. We had also noted in the previous submission that the trigeminal nucleus is weakly positive for peripherin, but that the staining pattern is uniform and not the type of axon bundle pattern that is seen in the inferior olive of other mammals. To us, this observation already argued against the presence of climbing fibers in the trigeminal nucleus. We also noted that the myelin stripes of the trigeminal nucleus were peripherin-antibody-negative. In the context of our olivo-cerebellar tract tracing we now also scrutinized the surroundings of the trigeminal nucleus for peripherin-antibody reactivity. We find that the ventral brainstem surrounding the trigeminal nucleus is devoid of peripherin-antibody reactivity. Accordingly, no climbing fibers, (which we have shown to be strongly peripherin-antibody-positive, see our point 1) arrive at the trigeminal nucleus. The absence of climbing fiber input indicates that previous work that identified the (trigeminal) nucleus as the inferior olive (Maseko et al 2013) is unlikely to be correct.

(4) We characterized the entry of the trigeminal nerve into the elephant brain.

To better understand how trigeminal information enters the elephant’s brain, we characterized the entry of the trigeminal nerve. This analysis indicated to us that the trigeminal nerve is not continuous with the olivo-cerebellar tract (the spinal trigeminal tract of Maseko et al. 2013) as previously claimed by Maseko et al. 2013. We show some of this evidence in Referee-Figure 1 below. The reason we think the trigeminal nerve is discontinuous with the olivo-cerebellar tract is the size discrepancy between the two structures. We first show this for the tracing data of Maseko et al. 2013. In the Maseko et al. 2013 data the trigeminal nerve (Referee-Figure 1A, their plate Y) has 3-4 times the diameter of the olivocerebellar tract (the alleged spinal trigeminal tract, Referee-Figure 1B, their plate Z). Note that most if not all trigeminal fibers are thought to continue from the nerve into the trigeminal tract (see our rat data below). We plotted the diameter of the trigeminal nerve and diameter of the olivo-cerebellar (the spinal trigeminal tract according to Maseko et al. 2013) from the Maseko et al. 2013 data (Referee-Figure 1C) and we found that the olivocerebellar tract has a fairly consistent diameter (46 ± 9 mm2, mean ± SD). Statistical considerations and anatomical evidence suggest that the tracing of the trigeminal nerve into the olivo-cerebellar (the spinal trigeminal tract according to Maseko et al. 2013) is almost certainly wrong. The most anterior point of the alleged spinal trigeminal tract has a diameter of 51 mm2 which is more than 15 standard deviations different from the most posterior diameter (194 mm2) of the trigeminal tract. For this assignment to be correct three-quarters of trigeminal nerve fibers would have to spontaneously disappear, something that does not happen in the brain. We also made similar observations in the African elephant Bibi, where the trigeminal nerve (Referee-Figure 1D) is much larger in diameter than the olivocerebellar tract (Referee-Figure 1E). We could also show that the olivocerebellar tract disappears into the peduncle posterior to where the trigeminal nerve enters (Referee-Figure 1F). Our data are very similar to Maseko et al. indicating that their outlining of structures was done correctly. What appears to have been oversimplified, is the assignment of structures as continuous. We also quantified the diameter of the trigeminal nerve and the spinal trigeminal tract in rats (from the Paxinos & Watson atlas; Referee-Figure 1D); as expected we found the trigeminal nerve and spinal trigeminal tract diameters are essentially continuous.

In our hands, the trigeminal nerve does not continue into a well-defined tract that could be traced after its entry. In this regard, it differs both from the olivo-cerebellar tract of the elephant or the spinal trigeminal tract of the rodent, both of which are well delineated. We think the absence of a well-delineated spinal trigeminal tract in elephants might have contributed to the putative tracing error highlighted in our Referee-Figure 1A-C.

We conclude that a size mismatch indicates trigeminal fibers do not run in the olivo-cerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013).

Author response image 1.

The trigeminal nerve is discontinuous with the olivo-cerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013)

A, Trigeminal nerve (orange) in the brain of African elephant LAX as delineated by Maseko et al. 2013 (coronal section; their plate Y).

B, Most anterior appearance of the spinal trigeminal tract of Maseko et al. 2013 (blue; coronal section; their plate Z). Note the much smaller diameter of the spinal trigeminal tract compared to the trigeminal nerve shown in C, which argues against the continuity of the two structures. Indeed, our peripherin-antibody staining showed that the spinal trigeminal tract of Maseko corresponds to the olivo-cerebellar tract and is discontinuous with the trigeminal nerve.

C, Plot of the trigeminal nerve and olivo-cerebellar tracts (the spinal trigeminal tract according to Maseko et al. 2013) diameter along the anterior-posterior axis. The trigeminal nerve is much larger in diameter than the olivocerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013). C, D measurements, for which sections are shown in panels C and D respectively. The olivocerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013) has a consistent diameter; data replotted from Maseko et al. 2013. At mm 25 the inferior olive appears.

D, Trigeminal nerve entry in the brain of African elephant Bibi; our data, coronal section, the trigeminal nerve is outlined in orange, note the large diameter.

E, Most anterior appearance of the olivo-cerebellar tract in the brain of African elephant Bibi; our data, coronal section, approximately 3 mm posterior to the section shown in A, the olivocerebellar tract is outlined in blue. Note the smaller diameter of the olivo-cerebellar tract compared to the trigeminal nerve, which argues against the continuity of the two structures.

F, Plot of the trigeminal nerve and olivo-cerebellar tract diameter along the anterior-posterior axis. The nerve and olivo-cerebellar tract are discontinuous and the trigeminal nerve is much larger in diameter than the olivocerebellar tract (the spinal trigeminal tract according to Maseko et al. 2013); our data. D, E measurements, for which sections are shown in panels D and E respectively. At mm 27 the inferior olive appears.

G, In the rat the trigeminal nerve is continuous in size with the spinal trigeminal tract. Data replotted from Paxinos and Watson.

Reviewer 2 (Public Review):

As indicated in my previous review of this manuscript (see above), it is my opinion that the authors have misidentified, and indeed switched, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex (Vsens). It is this specific point only that I will address in this second review, as this is the crucial aspect of this paper - if the identification of these nuclear complexes in the elephant brainstem by the authors is incorrect, the remainder of the paper does not have any scientific validity.

Comment: We agree with the referee that it is most important to sort out, the inferior olivary nuclear complex (IO) and the trigeminal nuclear complex, respectively.Change: We did additional experimental work to resolve this matter as detailed at the beginning of our response. Specifically, we ascertained that elephant climbing fibers are strongly peripherin-positive. Based on elephant climbing fiber peripherin-reactivity we delineated the elephant olivo-cerebellar tract. We find that the olivo-cerebellar connects to the structure we refer to as inferior olive to the cerebellum (the referee refers to this structure as the trigeminal nuclear complex). We also found that the trigeminal nucleus (the structure the referee refers to as inferior olive) appears to receive no climbing fibers. We provide indications that the tracing of the trigeminal nerve into the olivo-cerebellar tract by Maseko et al. 2023 was erroneous (Author response image 1). These novel findings support our ideas but are very difficult to reconcile with the referee’s partitioning scheme.

The authors, in their response to my initial review, claim that I "bend" the comparative evidence against them. They further claim that as all other mammalian species exhibit a "serrated" appearance of the inferior olive, and as the elephant does not exhibit this appearance, that what was previously identified as the inferior olive is actually the trigeminal nucleus and vice versa. 

For convenience, I will refer to IOM and VsensM as the identification of these structures according to Maseko et al (2013) and other authors and will use IOR and VsensR to refer to the identification forwarded in the study under review. <br /> The IOM/VsensR certainly does not have a serrated appearance in elephants. Indeed, from the plates supplied by the authors in response (Referee Fig. 2), the cytochrome oxidase image supplied and the image from Maseko et al (2013) shows a very similar appearance. There is no doubt that the authors are identifying structures that closely correspond to those provided by Maseko et al (2013). It is solely a contrast in what these nuclear complexes are called and the functional sequelae of the identification of these complexes (are they related to the trunk sensation or movement controlled by the cerebellum?) that is under debate.

Elephants are part of the Afrotheria, thus the most relevant comparative data to resolve this issue will be the identification of these nuclei in other Afrotherian species. Below I provide images of these nuclear complexes, labelled in the standard nomenclature, across several Afrotherian species. 

(A) Lesser hedgehog tenrec (Echinops telfairi) 

Tenrecs brains are the most intensively studied of the Afrotherian brains, these extensive neuroanatomical studies undertaken primarily by Heinz Künzle. Below I append images (coronal sections stained with cresol violet) of the IO and Vsens (labelled in the standard mammalian manner) in the lesser hedgehog tenrec. It should be clear that the inferior olive is located in the ventral midline of the rostral medulla oblongata (just like the rat) and that this nucleus is not distinctly serrated. The Vsens is located in the lateral aspect of the medulla skirted laterally by the spinal trigeminal tract (Sp5). These images and the labels indicating structures correlate precisely with that provide by Künzle (1997, 10.1016, see his Figure 1K,L. Thus, in the first case of a related species, there is no serrated appearance of the inferior olive, the location of the inferior olive is confirmed through connectivity with the superior colliculus (a standard connection in mammals) by Künzle (1997), and the location of Vsens is what is considered to be typical for mammals. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report. 

Peer Review Image 1.

(B) Giant otter shrew (Potomogale velox) 

The otter shrews are close relatives of the Tenrecs. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see hints of the serration of the IO as defined by the authors, but we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Peer Response Image 2.

(C) Four-toed sengi (Petrodromus tetradactylus) 

The sengis are close relatives of the Tenrecs and otter shrews, these three groups being part of the Afroinsectiphilia, a distinct branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see vague hints of the serration of the IO (as defined by the authors), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report. 

Peer Response Image 3.

(D) Rock hyrax (Procavia capensis) 

The hyraxes, along with the sirens and elephants form the Paenungulata branch of the Afrotheria. Below I append images of cresyl violet (left column) and myelin (right column) stained coronal sections through the brainstem with the IO, Vsens and Sp5 labelled as per the standard mammalian anatomy. Here we see hints of the serration of the IO (as defined by the authors), but we also see evidence of a more "bulbous" appearance of subnuclei of the IO (particularly the principal nucleus), and we also see many myelin stripes across the IO. Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report. 

Peer Review Image 4.

(E) West Indian manatee (Trichechus manatus) 

The sirens are the closest extant relatives of the elephants in the Afrotheria. Below I append images of cresyl violet (top) and myelin (bottom) stained coronal sections (taken from the University of Wisconsin-Madison Brain Collection, https://brainmuseum.org, and while quite low in magnification they do reveal the structures under debate) through the brainstem with the IO, Vsens and Sp5 labelled as per standard mammalian anatomy. Here we see the serration of the IO (as defined by the authors). Vsens is located laterally and skirted by the Sp5. This is in agreement with the authors, as they propose that ONLY the elephants show the variations they report.

Peer Review Image 5.

These comparisons and the structural identification, with which the authors agree as they only distinguish the elephants from the other Afrotheria, demonstrate that the appearance of the IO can be quite variable across mammalian species, including those with a close phylogenetic affinity to the elephants. Not all mammal species possess a "serrated" appearance of the IO. Thus, it is more than just theoretically possible that the IO of the elephant appears as described prior to this study. 

So what about elephants? Below I append a series of images from coronal sections through the African elephant brainstem stained for Nissl, myelin, and immunostained for calretinin. These sections are labelled according to standard mammalian nomenclature. In these complete sections of the elephant brainstem, we do not see a serrated appearance of the IOM (as described previously and in the current study by the authors). Rather the principal nucleus of the IOM appears to be bulbous in nature. In the current study, no image of myelin staining in the IOM/VsensR is provided by the authors. However, in the images I provide, we do see the reported myelin stripes in all stains - agreement between the authors and reviewer on this point. The higher magnification image to the bottom left of the plate shows one of the IOM/VsensR myelin stripes immunostained for calretinin, and within the myelin stripes axons immunopositive for calretinin are seen (labelled with an arrow). The climbing fibres of the elephant cerebellar cortex are similarly calretinin immunopositive (10.1159/000345565). In contrast, although not shown at high magnification, the fibres forming the Sp5 in the elephant (in the Maseko description, unnamed in the description of the authors) show no immunoreactivity to calretinin. 

Peer Review Image 6.

Comment: We appreciate the referee’s additional comments. We concede the possibility that some relatives of elephants have a less serrated inferior olive than most other mammals. We maintain, however, that the elephant inferior olive (our Figure 1J) has the serrated appearance seen in the vast majority of mammals.

Change: None.

Peripherin Immunostaining 

In their revised manuscript the authors present immunostaining of peripherin in the elephant brainstem. This is an important addition (although it does replace the only staining of myelin provided by the authors which is unusual as the word myelin is in the title of the paper) as peripherin is known to specifically label peripheral nerves. In addition, as pointed out by the authors, peripherin also immunostains climbing fibres (Errante et al., 1998). The understanding of this staining is important in determining the identification of the IO and Vsens in the elephant, although it is not ideal for this task as there is some ambiguity. Errante and colleagues (1998; Fig. 1) show that climbing fibres are peripherin-immunopositive in the rat. But what the authors do not evaluate is the extensive peripherin staining in the rat Sp5 in the same paper (Errante et al, 1998, Fig. 2). The image provided by the authors of their peripherin immunostaining (their new Figure 2) shows what I would call the Sp5 of the elephant to be strongly peripherin immunoreactive, just like the rat shown in Errant et al (1998), and more over in the precise position of the rat Sp5! This makes sense as this is where the axons subserving the "extraordinary" tactile sensitivity of the elephant trunk would be found (in the standard model of mammalian brainstem anatomy). Interestingly, the peripherin immunostaining in the elephant is clearly lamellated...this coincides precisely with the description of the trigeminal sensory nuclei in the elephant by Maskeo et al (2013) as pointed out by the authors in their rebuttal. Errante et al (1998) also point out peripherin immunostaining in the inferior olive, but according to the authors this is only "weakly present" in the elephant IOM/VsensR. This latter point is crucial. Surely if the elephant has an extraordinary sensory innervation from the trunk, with 400 000 axons entering the brain, the VsensR/IOM should be highly peripherin-immunopositive, including the myelinated axon bundles?! In this sense, the authors argue against their own interpretation - either the elephant trunk is not a highly sensitive tactile organ, or the VsensR is not the trigeminal nuclei it is supposed to be. 

Comment: We made sure that elephant climbing fibers are strongly peripherin-positive (our revised Figure 2). As we noted in already our previous ms, we see weak diffuse peripherin-reactivity in the trigeminal nucleus (the inferior olive according to the referee), but no peripherin-reactive axon bundles (i.e. climbing fibers) that are seen in the inferior olive of other species. We also see no peripherin-reactive axon bundles (i.e. the olivo-cerebellar tract) arriving in the trigeminal nucleus as the tissue surrounding the trigeminal nucleus is devoid of peripherin-reactivity. Again, this finding is incompatible with the referee’s ideas. As far as we can tell, the trigeminal fibers are not reactive for peripherin in the elephant, i.e. we did not observe peripherin-reactivity very close to the nerve entry, but unfortunately, we did not stain for peripherin-reactivity into the nerve. As the referee alludes to the absence of peripherin-reactivity in the trigeminal tract is a difference between rodents and elephants.

Change: Our novel Figure 2.

Summary: 

(1) Comparative data of species closely related to elephants (Afrotherians) demonstrates that not all mammals exhibit the "serrated" appearance of the principal nucleus of the inferior olive. 

(2) The location of the IO and Vsens as reported in the current study (IOR and VsensR) would require a significant, and unprecedented, rearrangement of the brainstem in the elephants independently. I argue that the underlying molecular and genetic changes required to achieve this would be so extreme that it would lead to lethal phenotypes. Arguing that the "switcheroo" of the IO and Vsens does occur in the elephant (and no other mammals) and thus doesn't lead to lethal phenotypes is a circular argument that cannot be substantiated. 

(3) Myelin stripes in the subnuclei of the inferior olivary nuclear complex are seen across all related mammals as shown above. Thus, the observation made in the elephant by the authors in what they call the VsensR, is similar to that seen in the IO of related mammals, especially when the IO takes on a more bulbous appearance. These myelin stripes are the origin of the olivocerebellar pathway, and are indeed calretinin immunopositive in the elephant as I show. 

(4) What the authors see aligns perfectly with what has been described previously, the only difference being the names that nuclear complexes are being called. But identifying these nuclei is important, as any functional sequelae, as extensively discussed by the authors, is entirely dependent upon accurately identifying these nuclei. 

(4) The peripherin immunostaining scores an own goal - if peripherin is marking peripheral nerves (as the authors and I believe it is), then why is the VsensR/IOM only "weakly positive" for this stain? This either means that the "extraordinary" tactile sensitivity of the elephant trunk is non-existent, or that the authors have misinterpreted this staining. That there is extensive staining in the fibre pathway dorsal and lateral to the IOR (which I call the spinal trigeminal tract), supports the idea that the authors have misinterpreted their peripherin immunostaining.

(5) Evolutionary expediency. The authors argue that what they report is an expedient way in which to modify the organisation of the brainstem in the elephant to accommodate the "extraordinary" tactile sensitivity. I disagree. As pointed out in my first review, the elephant cerebellum is very large and comprised of huge numbers of morphologically complex neurons. The inferior olivary nuclei in all mammals studied in detail to date, give rise to the climbing fibres that terminate on the Purkinje cells of the cerebellar cortex. It is more parsimonious to argue that, in alignment with the expansion of the elephant cerebellum (for motor control of the trunk), the inferior olivary nuclei (specifically the principal nucleus) have had additional neurons added to accommodate this cerebellar expansion. Such an addition of neurons to the principal nucleus of the inferior olive could readily lead to the loss of the serrated appearance of the principal nucleus of the inferior olive, and would require far less modifications in the developmental genetic program that forms these nuclei. This type of quantitative change appears to be the primary way in which structures are altered in the mammalian brainstem. 

Comment: We still disagree with the referee. We note that our conclusions rest on the analysis of 8 elephant brainstems, which we sectioned in three planes and stained with a variety of metabolic and antibody stains and in which assigned two structures (the inferior olive and the trigeminal nucleus). Most of the evidence cited by the referee stems from a single paper, in which 147 structures were identified based on the analysis of a single brainstem sectioned in one plane and stained with a limited set of antibodies. Our synopsis of the evidence is the following.

(1) We agree with the referee that concerning brainstem position our scheme of a ventromedial trigeminal nucleus and a dorsolateral inferior olive deviates from the usual mammalian position of these nuclei (i.e. a dorsolateral trigeminal nucleus and a ventromedial inferior olive).

(2) Cytoarchitectonics support our partitioning scheme. The compact cellular appearance of our ventromedial trigeminal nucleus is characteristic of trigeminal nuclei. The serrated appearance of our dorsolateral inferior olive is characteristic of the mammalian inferior olive; we acknowledge that the referee claims exceptions here. To our knowledge, nobody has described a mammalian trigeminal nucleus with a serrated appearance (which would apply to the elephant in case the trigeminal nucleus is situated dorsolaterally).

(3) Metabolic staining (Cyto-chrome-oxidase reactivity) supports our partitioning scheme. Specifically, our ventromedial trigeminal nucleus shows intense Cyto-chrome-oxidase reactivity as it is seen in the trigeminal nuclei of trigeminal tactile experts.

(4) Isomorphism. The myelin stripes on our ventromedial trigeminal nucleus are isomorphic to trunk wrinkles. Isomorphism is a characteristic of somatosensory brain structures (barrel, barrelettes, nose-stripes, etc) and we know of no case, where such isomorphism was misleading.

(5) The large-scale organization of our ventromedial trigeminal nuclei in anterior-posterior repeats is characteristic of the mammalian trigeminal nuclei. To our knowledge, no such organization has ever been reported for the inferior olive.

(6) Connectivity analysis supports our partitioning scheme. According to our delineation of the elephant olivo-cerebellar tract, our dorsolateral inferior olive is connected via peripherin-positive climbing fibers to the cerebellum. In contrast, our ventromedial trigeminal nucleus (the referee’s inferior olive) is not connected via climbing fibers to the cerebellum.

Change: As discussed, we advanced further evidence in this revision. Our partitioning scheme (a ventromedial trigeminal nucleus and a dorsolateral inferior olive) is better supported by data and makes more sense than the referee’s suggestion (a dorsolateral trigeminal nucleus and a ventromedial inferior olive). It should be published.

Reviewer #3 (Public Review):

Summary: 

The study claims to investigate trunk representations in elephant trigeminal nuclei located in the brainstem. The researchers identify large protrusions visible from the ventral surface of the brainstem, which they examined using a range of histological methods. However, this ventral location is usually where the inferior olivary complex is found, which challenges the author's assertions about the nucleus under analysis. They find that this brainstem nucleus of elephants contains repeating modules, with a focus on the anterior and largest unit which they define as the putative nucleus principalis trunk module of the trigeminal. The nucleus exhibits low neuron density, with glia outnumbering neurons significantly. The study also utilizes synchrotron X-ray phase contrast tomography to suggest that myelin-stripe-axons traverse this module. The analysis maps myelin-rich stripes in several specimens and concludes that based on their number and patterning that they likely correspond with trunk folds; however this conclusion is not well supported if the nucleus has been misidentified. 

Comment: The referee provides a summary of our work. The referee also notes that the correct identification of the trigeminal nucleus is critical to the message of our paper.

Change: In line with these assessments we focused our revision efforts on the issue of trigeminal nucleus identification, please see our introductory comments and our response to Referee 2.

Strengths: 

The strength of this research lies in its comprehensive use of various anatomical methods, including Nissl staining, myelin staining, Golgi staining, cytochrome oxidase labeling, and synchrotron X-ray phase contrast tomography. The inclusion of quantitative data on cell numbers and sizes, dendritic orientation and morphology, and blood vessel density across the nucleus adds a quantitative dimension. Furthermore, the research is commendable for its high-quality and abundant images and figures, effectively illustrating the anatomy under investigation.

Comment: We appreciate this positive assessment.

Change: None

Weaknesses: 

While the research provides potentially valuable insights if revised to focus on the structure that appears to be inferior olivary nucleus, there are certain additional weaknesses that warrant further consideration. First, the suggestion that myelin stripes solely serve to separate sensory or motor modules rather than functioning as an "axonal supply system" lacks substantial support due to the absence of information about the neuronal origins and the termination targets of the axons. Postmortem fixed brain tissue limits the ability to trace full axon projections. While the study acknowledges these limitations, it is important to exercise caution in drawing conclusions about the precise role of myelin stripes without a more comprehensive understanding of their neural connections. 

Comment: We understand these criticisms and the need for cautious interpretation. As we noted previously, we think that the Elife-publishing scheme, where critical referee commentary is published along with our ms, will make this contribution particularly valuable.

Change: Our additional efforts to secure the correct identification of the trigeminal nucleus.

Second, the quantification presented in the study lacks comparison to other species or other relevant variables within the elephant specimens (i.e., whole brain or brainstem volume). The absence of comparative data to different species limits the ability to fully evaluate the significance of the findings. Comparative analyses could provide a broader context for understanding whether the observed features are unique to elephants or more common across species. This limitation in comparative data hinders a more comprehensive assessment of the implications of the research within the broader field of neuroanatomy. Furthermore, the quantitative comparisons between African and Asian elephant specimens should include some measure of overall brain size as a covariate in the analyses. Addressing these weaknesses would enable a richer interpretation of the study's findings. 

Comment: We understand, why the referee asks for additional comparative data, which would make our study more meaningful. We note that we already published a quantitative comparison of African and Asian elephant facial nuclei (Kaufmann et al. 2022). The quantitative differences between African and Asian elephant facial nuclei are similar in magnitude to what we observed here for the trigeminal nucleus, i.e. African elephants have about 10-15% more facial nucleus neurons than Asian elephants. The referee also notes that data on overall elephant brain size might be important for interpreting our data. We agree with this sentiment and we are preparing a ms on African and Asian elephant brain size. We find – unexpectedly given the larger body size of African elephants – that African elephants have smaller brains than Asian elephants. The finding might imply that African elephants, which have more facial nucleus neurons and more trigeminal nucleus trunk module neurons, are neurally more specialized in trunk control than Asian elephants.

Change: We are preparing a further ms on African and Asian elephant brain size, a first version of this work has been submitted.

Reviewer #4 (Public Review): 

Summary: 

The authors report a novel isomorphism in which the folds of the elephant trunk are recognizably mapped onto the principal sensory trigeminal nucleus in the brainstem. Further, they identifiy the enlarged nucleus as being situated in this species in an unusual ventral midline position. 

Comment: The referee summarizes our work.

Change: None.

Strengths: 

The identity of the purported trigeminal nucleus and the isomorphic mapping with the trunk folds is supported by multiple lines of evidence: enhanced staining for cytochrome oxidase, an enzyme associated with high metabolic activity; dense vascularization, consistent with high metabolic activity; prominent myelinated bundles that partition the nucleus in a 1:1 mapping of the cutaneous folds in the trunk periphery; near absence of labeling for the anti-peripherin antibody, specific for climbing fibers, which can be seen as expected in the inferior olive; and a high density of glia.

Comment: The referee again reviews some of our key findings.

Change: None. 

Weaknesses: 

Despite the supporting evidence listed above, the identification of the gross anatomical bumps, conspicuous in the ventral midline, is problematic. This would be the standard location of the inferior olive, with the principal trigeminal nucleus occupying a more dorsal position. This presents an apparent contradiction which at a minimum needs further discussion. Major species-specific specializations and positional shifts are well-documented for cortical areas, but nuclear layouts in the brainstem have been considered as less malleable. 

Comment: The referee notes that our discrepancy with referee 2, needs to be addressed with further evidence and discussion, given the unusual position of both inferior olive and trigeminal nucleus in the partitioning scheme and that the mammalian brainstem tends to be positionally conservative. We agree with the referee. We note that – based on the immense size of the elephant trigeminal ganglion (50 g), half the size of a monkey brain – it was expected that the elephant trigeminal nucleus ought to be exceptionally large.

Change: We did additional experimental work to resolve this matter: (i) We ascertained that elephant climbing fibers are strongly peripherin-positive. (ii) Based on elephant climbing fiber peripherin-reactivity we delineated the elephant olivo-cerebellar tract. We find that the olivo-cerebellar connects to the structure we refer to as inferior olive to the cerebellum. (iii) We also found that the trigeminal nucleus (the structure the referee refers to as inferior olive) appears to receive no climbing fibers. (iv) We provide indications that the tracing of the trigeminal nerve into the olivo-cerebellar tract by Maseko et al. 2023 was erroneous (Referee-Figure 1). These novel findings support our ideas.

Reviewer #5 (Public Review): 

After reading the manuscript and the concerns raised by reviewer 2 I see both sides of the argument - the relative location of trigeminal nucleus versus the inferior olive is quite different in elephants (and different from previous studies in elephants), but when there is a large disproportionate magnification of a behaviorally relevant body part at most levels of the nervous system (certainly in the cortex and thalamus), you can get major shifting in location of different structures. In the case of the elephant, it looks like there may be a lot of shifting. Something that is compelling is that the number of modules separated but the myelin bands correspond to the number of trunk folds which is different in the different elephants. This sort of modular division based on body parts is a general principle of mammalian brain organization (demonstrated beautifully for the cuneate and gracile nucleus in primates, VP in most of species, S1 in a variety of mammals such as the star nosed mole and duck-billed platypus). I don't think these relative changes in the brainstem would require major genetic programming - although some surely exists. Rodents and elephants have been independently evolving for over 60 million years so there is a substantial amount of time for changes in each l lineage to occur.

I agree that the authors have identified the trigeminal nucleus correctly, although comparisons with more out groups would be needed to confirm this (although I'm not suggesting that the authors do this). I also think the new figure (which shows previous divisions of the brainstem versus their own) allows the reader to consider these issues for themselves. When reviewing this paper, I actually took the time to go through atlases of other species and even look at some of my own data from highly derived species. Establishing homology across groups based only on relative location is tough especially when there appears to be large shifts in relative location of structures. My thoughts are that the authors did an extraordinary amount of work on obtaining, processing and analyzing this extremely valuable tissue. They document their work with images of the tissue and their arguments for their divisions are solid. I feel that they have earned the right to speculate - with qualifications - which they provide. 

Comment: The referee summarizes our work and appears to be convinced by the line of our arguments. We are most grateful for this assessment. We add, again, that the skeptical assessment of referee 2 will be published as well and will give the interested reader the possibility to view another perspective on our work.

Change: None. 

Recommendations for the authors: 

Reviewer #1 (Recommendations For The Authors):

With this manuscript being virtually identical to the previous version, it is possible that some of the definitive conclusions about having identified the elephant trigeminal nucleus and trunk representation should be moderated in a more nuanced manner, especially given the careful and experienced perspective from reviewers with first hand knowledge elephant neuroanatomy.

Comment: We agree that both our first and second revisions were very much centered on the debate of the correct identification of the trigeminal nucleus and that our ms did not evolve as much in other regards. This being said we agree with Referee 2 that we needed to have this debate. We also think we advanced important novel data in this context (the delineation of elephant olivo-cerebellar tract through the peripherin-antibody).

Changes: Our revised Figure 2. 

The peripherin staining adds another level of argument to the authors having identified the trigeminal brainstem instead of the inferior olive, if differential expression of peripherin is strong enough to distinguish one structure from the other.

Comment: We think we showed too little peripherin-antibody staining in our previous revision. We have now addressed this problem.

Changes: Our revised Figure 2, i.e. the delineation of elephant olivo-cerebellar tract through the peripherin-antibody).

There are some minor corrections to be made with the addition of Fig. 2., including renumbering the figures in the manuscript (e.g., 406, 521). 

I continue to appreciate this novel investigation of the elephant brainstem and find it an interesting and thorough study, with the use of classical and modern neuroanatomical methods.

Comment: We are thankful for this positive assessment.

Reviewer #2 (Recommendations For The Authors):

I do realise the authors are very unhappy with me and the reviews I have submitted. I do apologise if feelings have been hurt, and I do understand the authors put in a lot of hard work and thought to develop what they have; however, it is unfortunate that the work and thoughts are not correct. Science is about the search for the truth and sometimes we get it wrong. This is part of the scientific process and why most journals adhere to strict review processes of scientific manuscripts. As I said previously, the authors can use their data to write a paper describing and quantifying Golgi staining of neurons in the principal olivary nucleus of the elephant that should be published in a specialised journal and contextualised in terms of the motor control of the trunk and the large cerebellum of the elephant. 

Comment: We appreciate the referee’s kind words. Also, no hard feelings from our side, this is just a scientific debate. In our experience, neuroanatomical debates are resolved by evidence and we note that we provide evidence strengthening our identification of the trigeminal nucleus and inferior olive. As far as we can tell from this effort and the substantial evidence accumulated, the referee is wrong.

Reviewer #4 (Recommendations For The Authors):

As a new reviewer, I have benefited from reading the previous reviews and Author response, even while having several new comments to add. 

(1) The identification of the inferior olive and trigeminal nuclei is obviously center stage. An enlargement of the trigeminal nuclei is not necessarily problematic, given the published reports on the dramatic enlargement of the trigeminal nerve (Purkart et al., 2022). At issue is the conspicuous relocation of the trigeminal nuclei that is being promoted by Reveyaz et al. Conspicuous rearrangements are not uncommon; for example, primary sensory cortical fields in different species (fig. 1 in H.H.A. Oelschlager for dolphins; S. De Vreese et al. (2023) for cetaceans, L. Krubitzer on various species, in the context of evolution). The difficult point here concerns what looks like a rather conspicuous gross anatomical rearrangement, in BRAINSTEM - the assumption being that the brainstem bauplan is going to be specifically conservative and refractory to gross anatomical rearrangement. 

Comment: We agree with the referee that the brainstem rearrangements are unexpected. We also think that the correct identification of nuclei needs to be at the center of our revision efforts.

Change: Our revision provided further evidence (delineation of the olivo-cerebellar tract, characterization of the trigeminal nerve entry) about the identity of the nuclei we studied.

Why would a major nucleus shift to such a different location? and how? Can ex vivo DTI provide further support of the correct identification? Is there other "disruption" in the brainstem? What occupies the traditional position of the trigeminal nuclei? An atlas-equivalent coronal view of the entire brainstem would be informative. The Authors have assembled multiple criteria to support their argument that the ventral "bumps" are in fact a translocated trigeminal principal nucleus: enhanced CO staining, enhanced vascularization, enhanced myelination (via Golgi stains and tomography), very scant labeling for a climbing fiber specific antibody ( anti-peripherin), vs. dense staining of this in the alternative structure that they identify as IO; and a high density of glia. Admittedly, this should be sufficient, but the proposed translocation (in the BRAINSTEM) is sufficiently startling that this is arguably NOT sufficient. <br /> The terminology of "putative" is helpful, but a more cogent presentation of the results and more careful discussion might succeed in winning over at least some of a skeptical readership. 

Comment: We do not know, what led to the elephant brainstem rearrangements we propose. If the trigeminal nuclei had expanded isometrically in elephants from the ancestral pattern, one would have expected a brain with big lateral bumps, not the elephant brain with its big ventromedial bumps. We note, however, that very likely the expansion of the elephant trigeminal nuclei did not occur isometrically. Instead, the neural representation of the elephant nose expanded dramatically and in rodents the nose is represented ventromedially in the brainstem face representation. Thus, we propose a ‘ventromedial outgrowth model’ according to which the elephant ventromedial trigeminal bumps result from a ventromedially direct outgrowth of the ancestral ventromedial nose representation.

We advanced substantially more evidence to support our partitioning scheme, including the delineation of the olivo-cerebellar tract based on peripherin-reactivity. We also identified problems in previous partitioning schemes, such as the claim that the trigeminal nerve continues into the ~4x smaller olivocerebellar tract (Referee-Figure 1C, D); we think such a flow of fibers, (which is also at odds with peripherin-antibody-reactivity and the appearance of nerve and olivocerebellar tract), is highly unlikely if not physically impossible. With all that we do not think that we overstate our case in our cautiously presented ms.

Change: We added evidence on the identification of elephant trigeminal nuclei and inferior olive.

(2) Role of myelin. While the photos of myelin are convincing, it would be nice to have further documentation. Gallyas? Would antibodies to MBP work? What is the myelin distribution in the "standard" trigeminal nuclei (human? macaque or chimpanzee?). What are alternative sources of the bundles? Regardless, I think it would be beneficial to de-emphasize this point about the role of myelin in demarcating compartments. <br /> I would in fact suggest an alternative (more neutral) title that might highlight instead the isomorphic feature; for example, "An isomorphic representation of Trunk folds in the Elephant Trigeminal Nucleus." The present title stresses myelin, but figure 1 already focuses on CO. Additionally, the folds are actually mentioned almost in passing until later in the manuscript. I recommend a short section on these at the beginning of the Results to serve as a useful framework.

Here I'm inclined to agree with the Reviewer, that the Authors' contention that the myelin stipes serve PRIMARILY to separate trunk-fold domains is not particularly compelling and arguably a distraction. The point can be made, but perhaps with less emphasis. After all, the fact that myelin has multiple roles is well-established, even if frequently overlooked. In addition, the Authors might make better use of an extensive relevant literature related to myelin as a compartmental marker; for example, results and discussion in D. Haenelt....N. Weiskopf (eLife, 2023), among others. Another example is the heavily myelinated stria of Gennari in primate visual cortex, consisting of intrinsic pyramidal cell axons, but where the role of the myelination has still not been elucidated. 

Comment: (1) Documentation of myelin. We note that we show further identification of myelinated fibers by the fluorescent dye fluomyelin in Figure 4B. We also performed additional myelin stains as the gold-myelin stain after the protocol of Schmued (Referee-Figure 2). In the end, nothing worked quite as well to visualize myelin-stripes as the bright-field images shown in Figure 4A and it is only the images that allowed us to match myelin-stripes to trunk folds. Hence, we focus our presentation on these images.

(2) Title: We get why the referee envisions an alternative title. This being said, we would like to stick with our current title, because we feel it highlights the major novelty we discovered.

(3) We agree with many of the other comments of the referee on myelin phenomenology. We missed the Haenelt reference pointed out by the referee and think it is highly relevant to our paper

Change: 1. Referee Figure. 2. Inclusion of the Haenelt-reference.

Author response image 2.

Myelin stripes of the elephant trunk module visualized by Gold-chloride staining according to Schmued

A, Low magnification micrograph of the trunk module of African elephant Indra stained with AuCl according to Schmued. The putative finger is to the left, proximal is to the right. Myelin stripes can easily be recognized. The white box indicates the area shown in B.

B, high magnification micrograph of two myelin stripes. Individual gold-stained (black) axons organized in myelin stripes can be recognized.

Schmued, L. C. (1990). A rapid, sensitive histochemical stain for myelin in frozen brain sections. Journal of Histochemistry & Cytochemistry, 38(5), 717-720.

Are the "bumps" in any way "analogous" to the "brain warts" seen in entorhinal areas of some human brains (G. W. van Hoesen and A. Solodkin (1993)? 

Comment: We think this is a similar phenomenon.

Change: We included the Hoesen and A. Solodkin (1993) reference in our discussion.

At least slightly more background (ie, a separate section or, if necessary, supplement) would be helpful, going into more detail on the several subdivisions of the ION and if these undergo major alterations in the elephant.

Comment: The strength of the paper is the detailed delineation of the trunk module, based on myelin stripes and isomorphism. We don’t think we have strong evidence on ION subdivisions, because it appears the trigeminal tract cannot be easily traced in elephants. Accordingly, we find it difficult to add information here.

Change: None.

Is there evidence from the literature of other conspicuous gross anatomical translocations, in any species, especially in subcortical regions? 

Comment: The best example that comes to mind is the star-nosed mole brainstem. There is a beautiful paper comparing the star-nosed mole brainstem to the normal mole brainstem (Catania et al 2011). The principal trigeminal nucleus in the star-nosed mole is far more rostral and also more medial than in the mole; still, such rearrangements are minor compared to what we propose in elephants.

Catania, Kenneth C., Duncan B. Leitch, and Danielle Gauthier. "A star in the brainstem reveals the first step of cortical magnification." PloS one 6.7 (2011): e22406.

Change: None.

(3) A major point concerns the isomorphism between the putative trigeminal nuclei and the trunk specialization. I think this can be much better presented, at least with more discussion and other examples. The Authors mention about the rodent "barrels," but it seemed strange to me that they do not refer to their own results in pig (C. Ritter et al., 2023) nor the work from Ken Catania, 2002 (star-nosed mole; "fingerprints in the brain") or other that might be appropriate. I concur with the Reviewer that there should be more comparative data. 

Comment: We agree.

Change: We added a discussion of other isomorphisms including the the star-nosed mole to our paper.

(4) Textual organization could be improved. 

The Abstract all-important Introduction is a longish, semi "run-on" paragraph. At a minimum this should be broken up. The last paragraph of the Introduction puts forth five issues, but these are only loosely followed in the Results section. I think clarity and good organization is of the upmost importance in this manuscript. I recommend that the Authors begin the Results with a section on the trunk folds (currently figure 5, and discussion), continue with the several points related to the identification of the trigeminal nuclei, and continue with a parallel description of ION with more parallel data on the putative trigeminal and IO structures (currently referee Table 1, but incorporate into the text and add higher magnification of nucleus-specific cell types in the IO and trigeminal nuclei). Relevant comparative data should be included in the Discussion.

Comment: 1. We agree with the referee that our abstract needed to be revised. 2. We also think that our ms was heavily altered by the insertion of the new Figure 2, which complemented Figure 1 from our first submission and is concerned with the identification of the inferior olive. From a standpoint of textual flow such changes were not ideal, but the revisions massively added to the certainty with which we identify the trigeminal nuclei. Thus, although we are not as content as we were with the flow, we think the ms advanced in the revision process and we would like to keep the Figure sequence as is. 3. We already noted above that we included additional comparative evidence.

Change: 1. We revised our abstract. 2. We added comparative evidence.

Reviewer #5 (Recommendations For The Authors): 

The data is invaluable and provides insights into some of the largest mammals on the planet. 

Comment: We are incredibly thankful for this positive assessment.

Author response:

Reviewer #3 (Public Review):

(1) Conditions on growth and interaction rates for feasibility and stability. The authors approach this using a mean field approximation, and it is important to note that there is no particular temperature dependence assumed here: as far as it goes, this analysis is completely general for arbitrary Lotka-Volterra interactions.

However, the starting point for the authors' mean field analysis is the statement that "it is not possible to meaningfully link the structure of species interactions to the exact closed-form analytical solution for [equilibria] 𝑥^*_𝑖 in the Lotka-Volterra model.

I may be misunderstanding, but I don't agree with this statement. The time-independent equilibrium solution with all species present (i.e. at non-zero abundances) takes the form

x^* = A^{-1}r

where A is the inverse of the community matrix, and r is the vector of growth rates. The exceptions to this would be when one or more species has abundance = 0, or A is not invertible. I don't think the authors intended to tackle either of these cases, but maybe I am misunderstanding that.

So to me, the difficulty here is not in writing a closed-form solution for the equilibrium x^*, it is in writing the inverse matrix as a nice function of the entries of the matrix A itself, which is where the authors want to get to. In this light, it looks to me like the condition for feasibility (i.e. that all x^* are positive, which is necessary for an ecologically-interpretable solution) is maybe an approximation for the inverse of A---perhaps valid when off-diagonal entries are small. A weakness then for me was in understanding the range of validity of this approximation, and whether it still holds when off-diagonal entries of A (i.e. inter-specific interactions) are arbitrarily large. I could not tell from the simulation runs whether this full range of off-diagonal values was tested.

We thank the reviewer for pointing this out and we agree that the language used is imprecise. The GLV model is solvable using the matrix inversion method but as they note, this does not give an interpretable expression in terms of the system parameters. This is important as we aim to build understanding of how these parameters (which in turn depend on temperature) affect the richness in communities. We have made this clearer in lines 372-379.

In regards to the validity of the approximation we have significantly increased the detail of the method in the manuscript, including the assumptions it makes (lines 384-393). In general the method assumes that any individual interaction has a weak effect on abundance. This will fail when the variation in interactions becomes too strong but should be robust to changes in the average interaction strength across the community.

As a secondary issue here, it would have been helpful to understand whether the authors' feasible solutions are always stable to small perturbations. In general, I would expect this to be an additional criterion needed to understand diversity, though as the authors point out there are certain broad classes of solutions where feasibility implies stability.

As the reviewer notes previous work using the GLV model by ? has shown that stability almost surely implies stability in the GLV. Thus we expect that our richness estimates derived from feasibility will closely resemble those from stabiltiy. We have amended the maintext to make this argument clear on lines 321-335.

(2) I did not follow the precise rationale for selecting the temperature dependence of growth rate and interaction rates, or how the latter could be tested with empirical data, though I do think that in principle this could be a valuable way to understand the role of temperature dependence in the Lotka-Volterra equations.

First, as the authors note, "the temperature dependence of resource supply will undoubtedly be an important factor in microbial communities"

Even though resources aren't explicitly modeled here, this suggests to me that at some temperatures, resource supply will be sufficiently low for some species that their growth rates will become negative. For example, if temperature dependence is such that the limiting resource for a given species becomes too low to balance its maintenance costs (and hence mortality rate), it seems that the net growth rate will be negative. The alternative would be that temperature affects resource availability, but never such that a limiting resource leads to a negative growth rate when a taxon is rare.

On the other hand, the functional form for the distribution of growth rates (eq 3) seems to imply that growth rates are always positive. I could imagine that this is a good description of microbial populations in a setting where the resource supply rate is controlled independently of temperature, but it wasn't clear how generally this would hold.

We thank the reviewer for their comment. The assumption of positive growth rates is indeed a feature of the Boltzmann-Arrhenius model of temperature dependence. We use the Boltzmann-Arrhenius model due to the dependence of growth on metabolic rate. As metabolic rate is ultimately determined by biochemical kinetics its temper- ature dependence is well described by the Boltzmann-Arrhenius. In addition to this reasoning there is a wealth of empirical evidence supporting the use of the Boltzmann- Arrhenius to describe the temperature dependence of growth rate in microbes.

Ultimately the temperature dependence of resource supply is not something we can directly consider in our model. As such we have to assume that resource supply is sufficient to maintain positive growth rates in the community. Note that this assump- tion only requires resource supply is sufficient to maintain positive growth rates (i.e. the maximal growth rate of species in isolation) not that resource supply is sufficient to maintain growth in the presence of intra- and interspecific competition. We have updated the manuscript in lines 156-159 to make these assumptions more clear.

Secondly, while I understand that the growth rate in the exponential phase for a single population can be measured to high precision in the lab as a function of temperature, the assumption for the form of the interaction rates' dependence on temperature seems very hard to test using empirical data. In the section starting L193, the authors seem to fit the model parameters using growth rate dependence on temperature, but then assume that it is reasonable to "use the same thermal response for growth rates and interactions". I did not follow this, and I think a weakness here is in not providing clear evidence that the functional form assumed in Equation (4) actually holds.

The reviewer is correct, it is very difficult to measure interaction coefficients experi- mentally and to our knowledge there is little to no data available on their empirical temperature responses. We as a best guess use the observed variation in thermal physiology parameters for growth rate as a proxy assuming that interactions must also depend on metabolic rates of the interacting species (see also response to com- ment 8).

eLife assessment

This important study builds on a previous publication, demonstrating that T. brucei has a continuous endomembrane system, which probably facilitates high rates of endocytosis. Using a range of cutting-edge approaches, the authors present compelling evidence that an actomyosin system, with the myosin TbMyo1 as an active molecular motor, is localized close to and can associate with the endosomal system in the bloodstream form of Trypanosoma brucei. It shows convincingly that both actin and Myo I play a role in the organization and integrity of the endosomal system: both RNAi-mediated depletion of Myo1, and treatment of the cells with latrunculin A resulted in endomembrane disruption. This work should be of interest to cell biologists and microbiologists working on the cytoskeleton, and unicellular eukaryotes.

Reviewer #1 (Public Review):

Using a combination of cutting-edge high-resolution technologies (expansion microscopy, SIM, and CLEM) and biochemical approaches (in vitro translocation of actin filaments, cargo uptake assays, and drug treatment), the authors revisit and update previous results about TbMyo1 and TbACT in the bloodstream form (BSF) of Trypanosoma brucei. They show that a great part of the myosin motor is cytoplasmic but the fraction associated with organelles is in proximity to the endosomal system and in glycosomes. In addition, they show that TbMyo1 can move actin filaments in vitro and visualize for the first time this actomyosin system using specific antibodies, a "classical" antibody for TbMyo1, and a chromobody for actin. Finally, using latrunculin A, which sequesters G-actin and prevents F-actin assembly, the authors show the delocalization and eventually the loss of the filamentous actin signal and the concomitant loss of the endosomal system integrity.<br /> Overall this well-conducted and convincing study paves the way toward the elucidation of the role of an actomyosin system in the maintenance of the endosomal network in T. brucei.

Strengths:

The work is of high quality and uses advanced technologies to determine the involvement TbMyo1 and actin in the integrity of the endosomal system. The conclusions are not over-interpreted and are supported by the experimental results and their quantification.

Weaknesses:

Although disruption of the actomyosin system using either the actin-depolymerizing drug latrunculin A or the TbMyo1-RNAi cell line established an effect on the endosomal system integrity, it remains to understand how this occurs mechanistically and what are the intracellular components involved.

Reviewer #2 (Public Review):

The study by Link et al. advances our understanding of the actomyosin system in T. brucei, focusing on the role of TbMyo1, a class I myosin, within the parasite's endosomal system. Using a combination of biochemical fractionation, in vitro motility assays, and advanced imaging techniques such as correlative light and electron microscopy (CLEM), this paper demonstrates that TbMyo1 is dynamically distributed across early and late endosomes, the cytosol, is associated with the cytoskeleton, and a fraction has an unexpected association with glycosomes. Notably, the study shows that TbMyo1 can translocate actin filaments at velocities suggesting an active role in intracellular trafficking, potentially higher than those observed for similar myosins in other cell types. This work not only elucidates the spatial dynamics of TbMyo1 within T. brucei but also suggests its broader involvement in maintaining the complex architecture of the endosomal network, underscoring the critical role of the actomyosin system in a parasite that relies on high rates of endocytosis for immune evasion.

A key strength of the study is its exceptional rigor and successful integration of a wide array of sophisticated techniques, such as in vitro motility assays, and advanced imaging methods, e.g. CLEM. This combination of approaches underscores the study's comprehensive approach to examining the ultrastructural organization of the trypanosome endomembrane system. The application of functional data using inhibitors, such as latrunculin A for actin depolymerization, further strengthens the study by providing insights into the dynamics and regulatory mechanisms of the endomembrane system. This demonstrates how the actomyosin system contributes to cellular morphology and trafficking processes. Furthermore, the discovery of TbMyo1 localization to glycosomes introduces a novel aspect to the potential roles of myosin I proteins within the cell, particularly in the context of organelles analogous to peroxisomes. This observation not only broadens our understanding of myosin I functionality but also opens up new avenues for research into the cell biology of trypanosomatids, marking a significant contribution to the field.

A significant initial weakness was the reliance on spatial association data to infer functional relationships without direct demonstration of biochemical activities in vivo. The authors have since addressed this by including new evidence from TbMyo1 RNAi cell lines and EM data that show the effects of TbMyo1 depletion on cellular ultrastructure. The authors' responses and additional data reinforce their initial conclusions and address previous concerns. Several new, elegant hypotheses are proposed in the discussion that warrant further investigation to fully understand TbMyo1's interactions and regulatory mechanisms in vivo.

Reviewer #3 (Public Review):

Summary:

In this work, Link and colleagues have investigated the localization and function of the actomyosin system in the parasite Trypanosoma brucei, which represents a highly divergent and streamlined version of this important cytoskeletal pathway. Using a variety of cutting-edge methods, the authors have shown that the T. brucei Myo1 homolog is a dynamic motor that can translocate actin, suggesting that it may not function as a more passive crosslinker. Using expansion microscopy, iEM, and CLEM, the authors show that MyoI localizes to the endosomal pathway, specifically the portion tasked with internalizing and targeting cargo for degradation, not the recycling endosomes. The glycosomes also appear to be associated with MyoI, which was previously not known. An actin chromobody was employed to determine the localization of filamentous actin in cells, which was correlated with the localization of Myo1. Interestingly, the pool of actomyosin was not always closely associated with the flagellar pocket region, suggesting that portions of the endolysomal system may remain at a distance from the sole site of parasite endocytosis. Lastly, the authors used actin-perturbing drugs to show that disrupting actin causes a collapse of the endosomal system in T. brucei, which they have shown recently does not comprise distinct compartments but instead a single continuous membrane system with subdomains containing distinct Rab markers.

Strengths:

Overall, the quality of the work is extremely high. It contains a wide variety of methods, including biochemistry, biophysics, and advanced microscopy that are all well deployed to answer the central question. The data is also well quantitated to provide additional rigor to the results. The main premise, that actomyosin is essential for the overall structure of the T. brucei endocytic system, is well supported and is of general interest, considering how uniquely configured this pathway is in this divergent eukaryote and how important it is to the elevated rates of endocytosis that are necessary for this parasite to inhabit its host.

Comments on revised version:

The revised manuscript has addressed the main issue, the lack of TbMyo1 functional data that was brought up during the first round of review. I find it interesting that Myo1 depletion has what appears to be a limited effect on endocytosis while producing a similar fragmentation of the endocytic pathway to what is seen with the LatA treatments. As CCV remains in both LatA treatments and TbMyo1 RNAi, it seems apparent that the organization of the endocytic pathway is not required for at least basal levels of endocytosis.

My other points were well addressed by the rebuttal. I am satisfied with the update.

Author response:

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

eLife assessment  

This important study builds on a previous publication (with partially overlapping authors), demonstrating that T. brucei has a continuous endomembrane system, which probably facilitates high rates of endocytosis. Using a range of cutting-edge approaches, the authors present compelling evidence that an actomyosin system, with the myosin TbMyo1 as the molecular motor, is localized close to the endosomal system in the bloodstream form (BSF) of Trypanosoma brucei. It shows convincingly that actin is important for the organization and integrity of the endosomal system, and that the trypanosome Myo1is an active motor that interacts with actin and transiently associates with endosomes, but a role of Myo1 in endomembrane function in vivo was not directly demonstrated. This work should be of interest to cell biologists and microbiologists working on the cytoskeleton, and unicellular eukaryotes.

We were delighted at the editors’ positive assessment and the reviewers’ rigorous, courteous, and constructive responses to the paper. We agree that a direct functional role for TbMyo1 in endomembrane activity was not demonstrated in the original submission, but have incorporated some new data (see new supplemental Figure S5) using the TbMyo1 RNAi cell line which are consistent with our earlier observations and interpretations.  

Public Reviews:   

Reviewer #1 (Public Review):  

Using a combination of cutting-edge high-resolution approaches (expansion microscopy, SIM, and CLEM) and biochemical approaches (in vitro translocation of actin filaments, cargo uptake assays, and drug treatment), the authors revisit previous results about TbMyo1 and TbACT in the bloodstream form (BSF) of Trypanosoma brucei. They show that a great part of the myosin motor is cytoplasmic but the fraction associated with organelles is in proximity to the endosomal system. In addition, they show that TbMyo1 can move actin filaments in vitro and visualize for the first time this actomyosin system using specific antibodies, a "classical" antibody for TbMyo1, and a chromobody for actin. Finally, using latrunculin A, which sequesters G-actin and prevents F-actin assembly, the authors show the delocalization and eventually the loss of the filamentous actin signal as well as the concomitant loss of the endosomal system integrity. However, they do not assess the localization of TbMyo1 in the same conditions.  

Overall the work is well conducted and convincing. The conclusions are not over-interpreted and are supported by the experimental results. 

We are very grateful to Reviewer1 for their balanced assessment. The reviewer is correct that we did not assess the localisation of TbMyo1 following latrunculin A treatment, but it is worth noting that Spitznagel et al. carried out this exact experiment in the earlier 2010 paper – we have mentioned this in the revised manuscript.  

Reviewer #2 (Public Review):  

Summary:  

The study by Link et al. advances our understanding of the actomyosin system in T. brucei, focusing on the role 

of TbMyo1, a class I myosin, within the parasite's endosomal system. Using a combination of biochemical fractionation, in vitro motility assays, and advanced imaging techniques such as correlative light and electron microscopy (CLEM), this paper demonstrates that TbMyo1 is dynamically distributed across early and late endosomes, the cytosol, is associated with the cytoskeleton, and a fraction has an unexpected association with glycosomes. Notably, the study shows that TbMyo1 can translocate actin filaments at velocities suggesting an active role in intracellular trafficking, potentially higher than those observed for similar myosins in other cell types. This work not only elucidates the spatial dynamics of TbMyo1 within T. brucei but also suggests its broader involvement in maintaining the complex architecture of the endosomal network, underscoring the critical role of the actomyosin system in a parasite that relies on high rates of endocytosis for immune evasion. 

Strengths:  

A key strength of the study is its exceptional rigor and successful integration of a wide array of sophisticated techniques, such as in vitro motility assays, and advanced imaging methods, including correlative light and electron microscopy (CLEM) and immuno-electron microscopy. This combination of approaches underscores the study's comprehensive approach to examining the ultrastructural organization of the trypanosome endomembrane system. The application of functional data using inhibitors, such as latrunculin A for actin depolymerization, further strengthens the study by providing insights into the dynamics and regulatory mechanisms of the endomembrane system. This demonstrates how the actomyosin system contributes to cellular morphology and trafficking processes. Furthermore, the discovery of TbMyo1 localization to glycosomes introduces a novel aspect to the potential roles of myosin I proteins within the cell, particularly in the context of organelles analogous to peroxisomes. This observation not only broadens our understanding of myosin I functionality but also opens up new avenues for research into the cellular biology of trypanosomatids, marking a significant contribution to the field. 

We are very pleased that the Reviewer felt the work is a significant contribution to the state of the art.  

Weaknesses:  

Certain limitations inherent in the study's design and scope render the narrative incomplete and make it challenging to reach definitive conclusions. One significant limitation is the reliance on spatial association data, such as colocalization of TbMyo1 with various cellular components-or the absence thereof-to infer functional relationships. Although these data suggest potential interactions, the authors do not confirm functional or direct physical interactions.  

While TbMyo1's localization is informative, the authors do not directly demonstrate its biochemical or mechanical activities in vivo, leaving its precise role in cellular processes speculative. Direct assays that manipulate TbMyo1 levels, activity, and/or function, coupled with observations of the outcomes on cellular processes, would provide more definitive evidence of the protein's specific roles in T. brucei. A multifaceted approach, including genetic manipulations, uptake assays, kinetic trafficking experiments, and imaging, would offer a more robust framework for understanding TbMyo1's roles. This comprehensive approach would elucidate not just the "what" and "where" of TbMyo1's function but also the "how" and "why," thereby deepening our mechanistic insights into T. brucei's biology.  

The reviewer is absolutely correct that the study lacks data on direct or indirect interactions between TbMyo1 and its intracellular partners, and this is an obvious area for future investigation. Given the generally low affinities of motor-cargo interactions, a proximity labelling approach (such has already been successfully used in studies of other myosins) would probably be the best way to proceed. 

The reviewer is also right to highlight that a detailed mechanistic understanding of TbMyo1 function in vivo is currently lacking. We feel that this would be beyond the scope of the present work, but have included some new data using the TbMyo1 RNAi cell line (Figure S5), which are consistent with our previous findings.  

Reviewer #3 (Public Review):  

Summary:  

In this work, Link and colleagues have investigated the localization and function of the actomyosin system in the parasite Trypanosoma brucei, which represents a highly divergent and streamlined version of this important cytoskeletal pathway. Using a variety of cutting-edge methods, the authors have shown that the T. brucei Myo1 homolog is a dynamic motor that can translocate actin, suggesting that it may not function as a more passive crosslinker. Using expansion microscopy, iEM, and CLEM, the authors show that MyoI localizes to the endosomal pathway, specifically the portion tasked with internalizing and targeting cargo for degradation, not the recycling endosomes. The glycosomes also appear to be associated with MyoI, which was previously not known. An actin chromobody was employed to determine the localization of filamentous actin in cells, which was correlated with the localization of Myo1. Interestingly, the pool of actomyosin was not always closely associated with the flagellar pocket region, suggesting that portions of the endolysomal system may remain at a distance from the sole site of parasite endocytosis. Lastly, the authors used actin-perturbing drugs to show that disrupting actin causes a collapse of the endosomal system in T. brucei, which they have shown recently does not comprise distinct compartments but instead a single continuous membrane system with subdomains containing distinct Rab markers.  

Strengths:  

Overall, the quality of the work is extremely high. It contains a wide variety of methods, including biochemistry, biophysics, and advanced microscopy that are all well-deployed to answer the central question. The data is also well-quantitated to provide additional rigor to the results. The main premise, that actomyosin is essential for the overall structure of the T. brucei endocytic system, is well supported and is of general interest, considering how uniquely configured this pathway is in this divergent eukaryote and how important it is to the elevated rates of endocytosis that are necessary for this parasite to inhabit its host.  

We are very pleased that the Reviewer formed such a positive impression of the work. 

Weaknesses:  

(1) Did the authors observe any negative effects on parasite growth or phenotypes like BigEye upon expression of the actin chromobody?  

Excellent question! There did appear to be detrimental effects on cell morphology in some cells, and it would definitely be worth doing a time course of induction to determine how quickly chromobody levels reach their maximum. The overnight inductions used here are almost certainly excessive, and shorter induction times would be expected to minimise any detrimental effects. We have noted these points in the Discussion.  

(2) The Garcia-Salcedo EMBO paper cited included the production of anti-actin polyclonal antibodies that appeared to work quite well. The localization pattern produced by the anti-actin polyclonals looks similar to the chromobody, with perhaps a slightly larger labeling profile that could be due to differences in imaging conditions. I feel that the anti-actin antibody labeling should be expressly mentioned in this manuscript, and perhaps could reflect differences in the F-actin vs total actin pool within cells.  

Implemented. We have explicitly mentioned the use of the anti-actin antibody in the Garcia-Salcedo paper in the revised Results and Discussion sections.  

(3) The authors showed that disruption of F-actin with LatA leads to disruption of the endomembrane system, which suggests that the unique configuration of this compartment in T. brucei relies on actin dynamics. What happens under conditions where endocytosis and endocyctic traffic is blocked, such as 4 C? Are there changes to the localization of the actomyosin components? 

Another excellent question! We did not analyse the localisation of TbMyo1 and actin under temperature block conditions, but this would definitely be a key experiment to do in follow-up work.

(4) Along these lines, the authors suggest that their LatA treatments were able to disrupt the endosomal pathway without disrupting clathrin-mediated endocytosis at the flagellar pocket. Do they believe that actin is dispensable in this process? That seems like an important point that should be stated clearly or put in greater context.  

Whether actin plays a direct or indirect role in endocytosis would be another fascinating question for future enquiry, and we do not have the data to do more than speculate on this point. Recent work in mammalian cells (Jin et al., 2022) has suggested that actin is primarily recruited when endocytosis stalls, and it could be that a similar role is at play here. We have noted this point in the Discussion. The observation of clathrin vesicles close to the flagellar pocket membrane and clathrin patches on the flagellar pocket membrane itself in the LatA-treated cells might suggest that some endocytic activity can occur in the absence of filamentous actin. 

Recommendations for the authors:

Note from the Reviewing Editor:  

During discussion, all reviewers agreed that the role of TbMyo1 in vivo in endomembrane function had not been directly demonstrated. This could be done by testing the endocytic trafficking of (for example) fluorophoreconjugated TfR and BSA in the existing Myo1 RNAi line, using wide-field microscopy. Examining the endosomes/lysosomes' organization by thin-section EM would be even better. The actin signal detected by the chromobody tends to occupy a larger region than the MyoI. It's therefore conceivable that actin filamentation and stabilization via other actin-interacting proteins create the continuous endosomal structure, while MyoI is necessary for transport or other related processes. 

These are all excellent points and very good suggestions. We have now incorporated new data (supplemental Figure S5) that includes BSA uptake assays in the TbMyo1 RNAi cell line and electron microscopy imaging after TbMyo1 depletion – the results are consistent with our earlier observations.   

Reviewer #1 (Recommendations For The Authors):  

-  Figure S2E. This panel is supposed to show the downregulation of TbMyo1 in the PCF compared to BSF but there is no loading control to support this claim. This is important because the authors mention in lines 381-383 that this finding conflicts with the previous study (Spitznagel et al., 2010). The authors also indicate in the figure legend that there is 50% less signal but there is no explanation about this quantification.   

Good point. Equal numbers of cells were loaded in each lane, but we did not have an antibody against a protein known to be expressed at the same level in both PCF and BSF cells to use as a loading control. Using a total protein stain would have been similarly unhelpful in this context, as the proteomes of PCF and BSF cells are dissimilar. The quantification was made by direct measurement after background subtraction, but without normalisation owing to the lack of a loading control. This makes the conclusion somewhat tentative, but given the large difference in signal observed between the two samples (and the fact that this is consistent with the proteomic data obtained by Tinti and Ferguson) we feel that the conclusion is valid. We have clarified these points in the figure legend and Discussion.  

-  It is mentioned in the discussion, as unpublished observations, that the predicted FYVE motif of TbMyo1 can bind specifically PI(3)P lipids. This is a very interesting point that would be new and would strengthen the suggested association with the endosomal system mainly based on imaging data. 

We agree that this is – potentially – a very exciting observation and it is an obvious direction for future enquiry.  

The data are preliminary at this stage and will form the basis of a future publication. Given that the predicted FYVE domain of TbMyo1 and known lipid-binding activity of other class I myosins makes this activity not wholly unexpected, we feel that it is acceptable at this stage to highlight these preliminary findings.  

-  The authors use the correlation coefficient to estimate the colocalization (lines 223-226). Although they clearly explain the difference between the correlation coefficient and the co-occurrence of two signals, I wonder if it would not be clearer for the audience to have quantification of the overlapping signals. Also, it is not mentioned on which images the correlation coefficient was measured. It seems that it is from widefield images (Figures 3E and 6E), and likely from SIM images for Figure 3C but the resolution is different. Are widefield images sufficient to assess these measurements? 

With hindsight, and given the different topological locations of TbMyo1 and the cargo proteins (cytosolic and lumenal, respectively) it would probably have been wiser to measure co-occurrence rather than correlation, but we would prefer not to repeat the entire analysis at this stage. The correlations were measured from widefield images using the procedure described in the Materials & Methods. These are obviously lower resolution than confocal or SIM images would be, but are still of value, we believe. One further point – upon re-examination of some of the TbMyo1 transferrin (Tf) and BSA data, we noticed that there are many pixels with a value of 0 for Tf/BSA and a nonzero value for TbMyo1 and vice-versa. The incidence of zero-versus-nonzero values in the two channels will have lowered the correlation coefficient, and in this sense, the correlation coefficients are giving us a hint of what the immuno-EM images later confirm: that the TbMyo1 and cargo are present in the same locations, but in different proportions. We have added this point to the discussion.  

-  It would be good to know if the loss of the endosomal system integrity (using EBI) is the same upon TbMyo1 depletion than in the latrunculin A treated parasites. 

We agree! We have now included new data (Figure S5) that suggests endosomal system morphology is altered upon TbMyo1 depletion. We would predict that the effect upon TbMyo1 depletion is slower or less dramatic than upon LatA treatment (as LatA affects both actin and TbMyo1, given that TbMyo1 depends upon actin for its localisation).

-  Conversely, it would be of interest to see how the localization of TbMyo1 changes upon latrunculin A treatment.

This experiment was done in 2010 by Spitznagel et al., who observed a delocalisation of the TbMyo1 signal after LatA treatment. We have noted this in the Results and Discussion.

Minor corrections:  

-  Line 374: Figure S1 should be Figure S2. 

Implemented (many thanks!).  

-  Panel E of Figure S2 refers to TbMyo1 and should therefore be included in Figure S1 and not S2. 

We would prefer not to implement this suggestion. We did struggle over the placing of this panel for exactly this reason, but as the samples were obtained as part of the experiments described in Figure S2, we felt that its placement here worked best in terms of the narrative of the manuscript.    

-  Figure S2F: the population of TbMyo21 +Tet seems lost after 48 h although the authors mention that there is no growth defect. 

Good eyes! We have re-added the panel, which shows that there was no growth defect in the tetracycline-treated population.  

Reviewer #2 (Recommendations For The Authors):  

Fig 1 vs. Figure 3: The biochemical fractionation experiments have been well-controlled, showing that 40% of TbMyo1 is found in both the cytosolic and cytoskeletal fractions, with only 20% in the organelle-associated fraction. The conclusion is supported by the experimental design, which includes controls to rule out crosscontamination between fractions. However, does this contrast with the widefield microscopy experiments, where the vast majority of the signal is in endocytic compartments and nowhere else? 

This is a good point. There are three factors that probably explain this. First, given that the actin cytoskeleton is associated with the endosomal system, a large proportion of the material partitioning into the cytoskeleton (P2) fraction is probably localised to the endosomal system (a fun experiment would be to repeat the fractionation with addition of ATP to the extraction buffer to make the myosin dissociate and see whether more appeared in the SN2 fraction as a result). Second, the 40% of the TbMyo1 that is cytosolic is distributed throughout the entire cellular volume, whereas the material localised to the endosomes is concentrated in a much smaller space, by comparison, and producing a stronger signal. Third, the widefield microscopy images have had brightness and contrast adjusted in order to reduce “background” signal, though this will also include cytosolic molecules. We hope these explanations are satisfactory, but would welcome any additional thoughts from either the reviewer or the community.  

The section title 'TbMyo1 translocates filamentous actin at 130 nm/s' could mislead readers by not specifying that the findings are from an in vitro experiment with a recombinant protein, which may not fully reflect the cell's complex context. Although this detail is noted in the figure legend, incorporating it into the main text and considering a title revision would ensure clarity and accuracy.  

Good point. Implemented – we have amended the section title to “TbMyo1 translocates filamentous actin at 130 nm/s in vitro” and the figure legend title to “TbMyo1 translocates filamentous actin in vitro”.  

The discussion of the translocation experiment could be better phrased addressing certain limitations. The in vitro conditions might not fully capture the complexity and dynamic nature of cellular environments where multiple regulatory mechanisms, interacting partners, and cellular compartments come into play. 

Good point, implemented. We have added a note on this to the Discussion.  

It is puzzling that RNAi, which is widely used in T. brucei was not used to further investigate the functional roles of TbMyo1 in Trypanosoma brucei. Given that the authors already had the cell line and used it to validate the specificity of the anti-TbMyo1. RNAi could have been employed to knock down TbMyo1 expression and observe the resultant effects on actin filament dynamics and organization within the cell. This would have directly tested TbMyo1's contribution to actin translocation observed in the in vitro experiments. 

It would obviously be interesting to carry out an in-depth characterisation of the phenotype following TbMyo1 depletion and whether this has an effect on actin dynamics. We have now included additional data (supplemental Figure S5) using the TbMyo1 RNAi cells and the results are consistent with our earlier observations and interpretations. It is worth noting too that at least for electron microscopy studies of intracellular morphology, the slower onset of an RNAi phenotype and the asynchronous replication of T. brucei populations make observation of direct (early) effects of depletion challenging – hence the preferential use of LatA here to depolymerise actin and trigger a faster phenotype.  

I found that several declarative statements within the main text may not be fully supported by the overall evidence. I suggest modifications to present a more balanced view,  

Line 227: "The results here suggest that although the TbMyo1 distribution overlaps with that of endocytic cargo, the signals are not strongly correlated." This conclusion about the lack of strong correlation might mislead readers about the functional relationship between TbMyo1 and endocytic cargo, as colocalization does not directly imply functional interaction. 

We would prefer not to alter this statement. It was our intention to phrase this cautiously, as we have not directly investigated the functional interplay between TbMyo1 and endocytic cargo and the subsequent sentence directs the reader to the Discussion for more consideration of this issue.    

Line 397: "This relatively high velocity might indicate that TbMyo1 is participating in intracellular trafficking of BSF T. brucei and functioning as an active motor rather than a static tether." The statement directly infers TbMyo1's functional role from in vitro motility assay velocities without in vivo corroboration.

We have amended the sentence in the Discussion to make it clear that it is speculative.  

The hypothesis that cytosolic TbMyo1 adopts an auto-inhibited "foldback" configuration, drawn by analogy with findings from other studies, is intriguing. Yet, direct evidence linking this configuration to TbMyo1's function in T. brucei is absent from the data presented. 

We have amended the sentence in the Discussion to make it clear that it is speculative. Future in vitro experiments will test this hypothesis directly.  

The suggestion that a large cytosolic fraction of TbMyo1 indicates dynamic behavior, high turnover on organelles, and a low duty ratio is plausible but remains speculative without direct experimental evidence. Measurements of TbMyo1 turnover rates or duty ratios in T. brucei through kinetic studies would substantiate this claim with the necessary evidence.  

We have amended the sentence in the Discussion to make it clear that it is speculative, and deleted the reference to a possible low duty ratio. Again, future in vitro experiments will measure the duty ratio of TbMyo1 using stopped-flow. 

Reviewer #3 (Recommendations For The Authors):  

Lines 171-172: The authors mention that MyoI could be functioning as a motor rather than a tether. The differences in myosin function have not been introduced prior to this. I would recommend explaining these differences and what it could mean for the function of the motor in the introduction to help a non-expert audience.

Good point. Implemented.  

Line 94-95: This phenotype only holds for the bloodstream form- the procyclic form are quite resistant to actin RNAi and MyoI RNAi. I would clarify. 

Good point. Implemented.  

Line 142-146: did the authors attempt to knock out the Myo21? 

Good point. No, this was not attempted. Given the extremely low expression levels of TbMyo21 in the BSF cells we would not expect a strong phenotype, but this assumption would be worth testing. 

Figure 3D: is there a reason why the authors chose to show the single-channel images in monochrome in this case?  

Not especially. These panels are the only ones that show a significant overlap in the signals between the two channels (unlike the colabelling experiments with ER, Golgi), so greyscale images were used because of their higher contrast. 

Line 397-398: I'm struggling a bit to understand how MyoI could be involved in intracellular trafficking in the endosomal compartments if the idea is that we have a continuous membrane? Some more detail as to the author's thinking here would be useful. 

Implemented. We have noted that this statement is speculative, and emphasised that being an active motor does not automatically mean that it is involved in intracellular traffic – it could instead be involved in manipulating endosomal membranes. We have noted too that the close proximity between TbMyo1 and the lysosome (Figures

3-5) could be important in this regard. The lysosome is not contiguous with the endosomal system, and it is possible that TbMyo1 is working as a motor to transport material (class II clathrin-coated vesicles) from the endosomal system to the lysosome.  

Line 493-496: Does this mean that endocytosis from the FP does not require actin? This would be hard to explain considering the phenotypes observed in the original actin RNAi work. Is the BigEye phentopye observed in BSF actin RNAi and Myo1 RNAi cells due to some indirect effect? 

It seems possible that actin is not directly or essentially involved in endocytosis, and the characterisation of the actin RNAi phenotype would be worth revisiting in this respect – we have noted this in the Discussion. Although RNAi of actin was lethal, the phenotype appears less penetrant than that seen following depletion of the essential endocytic cofactor clathrin (based on the descriptions in Garcia-Salcedo et al., 2004 and Allen et al., 2003). BigEye phenotypes occur in BSF cells whenever there is some perturbation of endomembrane trafficking and are not necessarily a direct consequence of depletion – this is why careful investigation of early timepoints following RNAi induction is critical.

Author response:

Reviewer #3 (Public Review):

The paper by Rai and colleagues examines the transcriptional response of Candida glabrata, a common human fungal pathogen, during interaction with macrophages. They use RNA PolII profiling to identify not just the total transcripts but instead focus on the actively transcribing genes. By examining the profile over time, they identify particular transcripts that are enriched at each timepoint, and build a hierarchical model for how a transcription factor, Xbp1, may regulate this response. Due to technical difficulties in identifying direct targets of Xbp1 during infection, the authors then turn to the targets of Xbp1 during cellular quiescence.

The authors have generated a large and potentially impactful dataset, examining the responses of C. glabrata during an important host-pathogen interface. However, the conclusions that the authors make are not well supported by the data. The ChIP-seq is interesting, but the authors make conclusions about the biological processes that are differentially regulated without testing them experimentally. Because Candida glabrata has a significant percent of the genome without GO term annotation, the GO term enrichment analysis is less useful than in a model organism. To support these claims, the authors should test the specific phenotypes, and validate that the transcriptional signature is observed at the protein level.

Additionally, the authors should also include images of the infections, along with measurements of phagocytosis, to show that the time points are the appropriate. At 30 minutes, are C. glabrata actually internalized or just associated? This may explain the difference in adherence genes at the early timepoint. For example, in Lines 123-132, the authors could measure the timing of ROS production by macrophages to determine when these attacks are deployed, instead of speculating based on the increased transcription of DNA damage response genes. Potentially, other factors could be influencing the expression of these proteins. At the late stage of infection, the authors should measure whether the C. glabrata cells are proliferating, or if they have escaped the macrophage, as other fungi can during infection. This may explain some of the increase in transcription of genes related to proliferation.

An additional limitation to the interpretation of the data is that the authors should put their work in the context of the existing literature on C. albicans temporal adaptation to macrophages, including recent work from Munoz (doi: 10.1038/s41467-019-09599-8), Tucey (doi: 10.1016/j.cmet.2018.03.019), and Tierney (doi: 10.3389/fmicb.2012.00085), among others.

When comparing the transcriptional profile between WT and xbp1 mutant, it is not clear whether the authors compared the strains under non-stress conditions. The authors should include an analysis of the wild-type to xbp1 mutants in the absence of macrophage stress, as the authors claims of precocious transcription may be a function of overall decreased transcriptional repression, even in the absence of the macrophage stress. The different cut-offs used to call peaks in the two strain backgrounds is also somewhat concerning-it is not clear to me whether that will obscure the transcriptional signature of each of the strains. Additionally, the authors go on to show that the xbp1 mutant has a significant proliferation defect in macrophages, so potentially this could confound the PolII binding sites if the cells are dying.

In the section on hierarchical analysis of transcription factors, at least one epistasis experiment should have been performed to validate the functional interaction between Xbp1 and a particular transcription factor. If the authors propose a specific motif, they should test this experimentally through EMSA assays to fully test that the motif is functional.

The jump from macrophages to quiescent culture is also not well justified. If the transcriptional program is so dynamic during a timecourse of macrophage infection, it is hard to translate the findings from a quiescent culture to this host environment.

Overall, there is a strong beginning and the focus on active transcription in the macrophage is an exciting approach. However, the conclusions need additional experimental evidence.

We thank this reviewer’s critical analysis of our manuscript and the comments.

We fully agree that the jump from macrophages to quiescent culture is also not well justified. We have successfully performed CgXbp1 ChIP-seq during macrophage infection and have rewritten the manuscript according to the new results. With the CgXbp1 ChIP-seq data during macrophage infection added, we have removed the data related to quiescence to focus the paper on the macrophage response. Because of this, we have also removed the DNA binding motif analysis from this work and will report the findings in a separate manuscript comparing CgXbp1 bindings between macrophage response and quiescence.

As mentioned above, the RNAPII ChIP-seq time course experiment compared RNAP occupancies at different times during infection to the first infection time point. We did not calculate relative to the data in the absence of stress (e.g. before infection), because Xbp1 was expressed at a low level and induced by stresses. Hence its role under no stress conditions is expected to be less than inside macrophages. In addition, up-regulation of its target genes depends on the presence of their transcriptional activators under the experimental conditions, which is going to be very different in normal growth media (RPMI or YPD; i.e. before infection) versus inside macrophages. Hence, comparing to normal growth media would not show the real CgXbp1 effects and/or the CgXbp1 effect might be different. In fact, this can be seen from the new RNAseq analysis of wildtype and Cgxbp1∆ C. glabrata cells in the presence and absence of fluconazole (which are added to the revised manuscript to study CgXbp1’s role on fluconazole resistance). The result shows that CgXbp1 (which was expressed at a low level) has a very small effect on global expression and the up-regulated genes are mainly related to transmembrane transport. More importantly, the effect of the Cgxbp1∆ mutant on TCA cycle and amino acid biosynthesis genes’ expression during macrophage infection is not observed when the mutant is grown under normal growth conditions (YPD without fluconazole). Therefore, the results show that CgXbp1 has condition-specific effects on global gene expression, which is also dependent on the transcriptional activators present in the cell. The result of the new RNAseq analysis of wildtype and Cgxbp1∆ C. glabrata cells in the absence of fluconazole is described in lines 329-339 as follows: “On the other hand, 135 genes were differentially expressed in the Cgxbp1∆ mutant during normal exponential growth (i.e. no fluconazole treatment) (Figure 6c) with up-regulated genes highly enriched with the “transmembrane transport” function and down- regulated genes associated with different metabolic processes (e.g. carbohydrate, glycogen and trehalose) (e.g. carbon metabolism, nucleotide metabolism, and transmembrane transport, etc.) (Supplementary Table 12). Interesting, the TCA cycle and amino acid biosynthesis genes, whose expressions were accelerated in the Cgxbp1∆ mutant during macrophage (Figure 3C, 3D), were not affected by the loss of CgXbp1 function under normal growth conditions (i.e. in YPD media without fluconazole) (Supplementary Figure 11, Supplementary Table 11), suggesting that the overall (direct and indirect) effects of CgXbp1 are condition-specific.”

For the comment about RNAPII bindings affected by dying cells, our observation of reduced proliferation does not mean that the cells were dying, because we did observe increase in cell numbers over time (i.e. the cells were proliferating) but the rate of proliferation was slower in the Cgxbp1∆ mutant comparing to wildtype. Presumably, the reduced proliferation and/or growth within macrophages is due to poorer adaptation in and compromised response to macrophages.

We have also discussed our findings in the context of the suggested (and other) literatures in various parts of the Discussion.

Reviewer #4 (Public Review):

Macrophages are the first line of defense against invading pathogens. C. glabrata must interact with these cells as do all pathogens seeking to establish an infection. Here, a ChIP-seq approach is used to measure levels of RNA polymerase II levels across Cg genes in a macrophage infection assay. Differential gene expression is analyzed with increasing time of infection. These differentially expressed genes are compared at the promoter level to identify potential transcription factors that may be involved in their regulation. A factor called CgXbp1 on the basis of its similar with the S. cerevisiae Xbp1 protein is characterized. ChIP-seq is done on CgXbp1 using in vitro grown cells and a potential binding site identified. Evidence is provided that CgXbp1 affects virulence in a Galleria system and that this factor might impact azole resistance.

As the authors point out, candidiasis associated with C. glabrata has dramatically increased in the recent past. Understanding the unique aspects of this Candida species would be a great value in trying to unravel the basis of the increasing fungal disease caused by C. glabrata. The use of ChIP-seq analysis to assess the time-dependent association of RNA polymerase II with Cg genes is a nice approach. Identification of CgXbp1 as a potential participant in the control of this gene expression program is also interesting. Unfortunately, this work suffers by comparison to a significant amount of previous effort that renders the progress detailed here incremental at best.

I agree that their ChIP-seq time course of RNA polymerase II distribution across the Cg genome is both elegant and an improvement on previous microarray experiments. However, these microarray experiments were carried out 14 years ago and while the current work is certainly at higher resolution, little more can be gleaned from the current work. The authors argue that standard transcriptional analysis is compromised by transcript stability effects. I would suggest that, while no approach is without issues, quite a bit has been learned from approaches like RNA-seq and there are recent developments to this technique that allow for a focus on newly synthesized mRNA (thiouridine labeling).

The CgXbp1 characterization relies heavily on work from S. cerevisiae. This is disappointing as conservation of functional links between C. glabrata and S. cerevisiae is not always predictable.

The effects caused by loss of CgXBP1 on virulence (Figure 4) may be statistically significant but are modest. No comparison is shown for another gene that has already been accepted to have a role in virulence to allow determination of the biological importance of this effect.

The phenotypic effects of the loss of XBP1 on azole resistance look rather odd (Figure 6). The appearance of fluconazole resistant colonies in the xbp1 null strain occurs at a very low frequency and seems to resemble the appearance of rho0 cells in the population. The vast majority of xbp1 null cells do not exhibit increased growth compared to wild-type in the presence of fluconazole.

Irrespective of the precise explanation, more analysis should be performed to confirm that CgXbp1 is negatively regulating the genes suggested in Figure 6A to be responsible for the increased fluconazole resistance.

Additionally, the entire analysis of CgXbp1 is based on ChIP-seq performed using cells grown under very different conditions that the RNA polymerase II study. Evidence should be provided that the presumptive CgXbp1 target genes actually impact the expression profiles established earlier.

We thank this reviewer’s critical analysis of our manuscript. We have done the following to address the comments. As a result, the manuscript is significantly improved.

• The ChIP-seq data of Xbp1 in macrophage has been successfully generated and the result is now presented in Figure 2C-2F, and lines 182-227 of the revised manuscript. With the addition, we have removed the ChIPseq data related to quiescent from the revised manuscript and re-written the manuscript focusing on the role of Xbp1 in macrophage.

• We agree that the conservation of functional links between C. glabrata and S. cerevisiae is not always predictable. That’s the reason why we did not solely rely on the S. cerevisiae network for inferring Xbp1’s functions, and had undertaken several different ways (e.g. ChIP-seq of Xbp1 and characterization of the Cgxbp1∆ mutant) to delineate its functions.

• We also agree that the virulence effect is modest, but it is, nevertheless, an effect that may contribute to the overall virulence of C. glabrata. Since virulence is a pleiotropic trait involving many genes and every gene affects different aspects of the complex process, we feel that it is not fair to penalize a given gene based on its (weaker) effect relative to another gene. Therefore, we respectfully disagree that another gene should be included for benchmarking the effect.

• We have measured C. glabrata cell numbers in a time course experiment. The result (presented in Figure 4A) showed that there was an increase in cell number at the end of the macrophage infection time course experiment (e.g. 8 hr). We have highlighted this information on lines 278-283.

• Additional analysis of the fluconazole resistance phenotype of the Cgxbp1∆ mutant has been added, including standard MIC assays. The results are presented in Figure 5C-5E.

• As suggested and to understand the role of CgXbp1 on fluconazole resistance, we have now carried out RNAseq analysis of WT and the Cgxbp1∆ mutant in the presence and absence of fluconazole. The genes differentially controlled in the Cgxbp1∆ mutant have been identified and a proposed model on how CgXbp1 affects fluconazole resistance is added to Figure 7 in the revised manuscript.

Author response:

Reviewer #1 (Public Review):

The authors conducted cross-species comparisons between the human brain and the macaque brain to disentangle the specific characteristics of structural development of the human brain. Although previous studies had revealed similarities and differences in brain anatomy between the two species by spatially aligning the brains, the authors made the comparison along the chronological axis by establishing models for predicting the chronological ages with the inputting brain structural features. The rationale is actually clear given that brain development occurs over time in both. More interestingly, the model trained on macaque data was better able to predict the age of humans than the human-trained model was at predicting macaque age. This revealed a brain cross-species age gap (BCAP) that quantified the discrepancy in brain development between the two species, and the authors even found this BCAP measure was associated with performance on behavioral tests in humans. Overall, this study provides important and novel insights into the unique characteristics of human brain development. The authors have employed a rigorous scientific approach, reflecting diligent efforts to scrutinize the patterns of brain age models across species. The clarity of the rationale, the interpretability of the methods, and the quality of the presentation all contribute to the strength of this work.

We are grateful to your helpful and thorough review and for being so positive about our manuscript. Following your recommendations, we have added more analytic details that have strengthened our paper. We would like to thank you for your input.

Reviewer #2 (Public Review):

In the current study, Li et al. developed a novel approach that aligns chronological age to a cross-species brain age prediction model to investigate the evolutionary effect. This method revealed some interesting findings, like the brain-age gap of the macaque model in predicting human age will increase as chronological age increases, suggesting an evolutionary alignment between the macaque brain and the human brain in the early stage of development. This study exhibits ample novelty and research significance. However, I still have some concerns regarding the reliability of the current findings.

We thank you for the positive and appreciative feedback on our work and the insightful comments, which we have addressed below.

Question 1: Although the authors named their new method a "cross-species" model, the current study only focused on the prediction between humans and macaques. It would be better to discuss whether their method can also generalize to cross-species examination of other species (e.g., C. elegans), which may provide more comprehensive evolutionary insights. Also, other future directions with their new method are worth discussing.

We appreciate your insightful comment regarding the generalizability of our model to other species. As you said, we indeed only performed human-macaque cross-species study not including other species. In our study, we only focused human and macaque because macaque is considered to be one of the closest primates to humans except chimpanzees and thus is considered to be the best model for studying human brain evolution. However, our proposed method has limitations that limit its generalizability for other species, e.g., C. elegans. First, our model was trained using MRI data, which limits its applicability to species for which such data is unavailable. This technological requirement brings a barrier to broaden cross-species application. Second, our current model is based on homologous brain atlases that are available for both humans and macaques. The lack of comparable atlases for other species further restricts the model's generalizability. We have discussed this limitation in the revised manuscript and outlined potential future directions to overcome these challenges. This includes discussing the need for developing comparable imaging techniques and standardized brain atlases across a wider range of species to enhance the model's applicability and broaden our understanding of cross-species neurodevelopmental patterns.

On page 15, lines 11-18

“However, the existing limitation should be noted regarding the generalizability of our proposed approach for cross-species brain comparison. Our current model relies on homologous brain atlases, and the lack of comparable atlases for other species restricts its broader applicability. To address this limitation, future research should focus on developing prediction models that do not depend on atlases. For instance, 3D convolutional neural networks could be trained directly on raw MRI data for age prediction. These deep learning models may offer greater flexibility for cross-species applications once the training within species is complete. Such advancements would significantly enhance the model's adaptability and expand its potential for comparative neuroscience studies across a wider range of species.”

Question 2: Algorithm of prediction model. In the method section, the authors only described how they chose features, but did no description about the algorithm (e.g., supporting vector regression) they used. Please add relevant descriptions to the methods.

Thank you for your comment. We apologize for not providing sufficient details about the model training process in our initial submission. In our study, we used a linear regression model for prediction. We have provided more details regarding the algorithm of prediction model in our response to Reviewer #1. For your convenience, we have attached them below.

For details on the algorithm of prediction model:

“A linear regression model was adopted for intra- and inter-species age prediction. The linear regression model was built including the following three main steps: 1) Feature selection: a total of two steps are required to extract the final features. The first step is preliminary extraction. First, all the human or macaque participants were divided into 10-fold and 9-fold was used for model training and 1-fold for model test. The preliminary features were chosen by identifying the significantly age-associated features with p < 0.01 during calculating Pearson’s correlation coefficients between all the 260 features and actual ages of the 9-fold subjects. This process was repeated 100 times. Since we obtained not exactly the same preliminary features each time, we thus further analyzed the preliminary features using two methods to determine the final features: common features and minimum mean absolute error (min MAE). Common features are the preliminary features that were selected in all the 100 times during preliminary model training. The min MAE features were the preliminary features that with the smallest MAE value during the 100 times model test for predicting age. After the above feature selections, we obtained two sets of features: 62 macaque features and 225 human features (common features) and 117 macaque features and 239 human features (min MAE). In addition, to further exclude the influences of unequal number of features in human and macaque, we also selected the first 62 features in human and macaque to test the model prediction performances. 2) Model construction: we conducted age prediction linear model using 10-fold cross-validation based on the selected features for human and macaque separately. The linear model parameters are obtained using the training set data and applied to the test set for prediction. The above process is also repeated 100 times. 3) Prediction: with the above results, we obtained the optimal linear prediction models for human and macaque. Next, we performed intra-species and inter-species brain age prediction, i.e., human model predicted human age, human model predicted macaque age, macaque model predicted macaque age and macaque model predicted human age. Three sets of features (62 macaque features and 225 human features; 117 macaque features and 239 human features; 62 macaque features and 62 human features) were used to test the prediction models for cross-validation and to exclude effects of different number of features in human and macaque. In the main text, we showed the results of brain age prediction, brain developmental and evolutional analyses based on common features and the results obtained using other two types of features were shown in supplementary materials. The prediction performances were evaluated by calculating the Pearson’s correlation and MAE between actual ages and predicted ages.”

Question 3: Sex difference. The sex difference results are strange to me. For example, in the second row of Figure Supplement 3A, different models show different correlation patterns, but why their Pearson's r is all equal to 0.3939? If they are only typo errors, please correct them. The authors claimed that they found no sex difference. However, the results in Figure Supplement 3 show that, the female seems to have poorer performance in predicting macaque age from the human model. Moreover, accumulated studies have reported sex differences in developing brains (Hines, 2011; Kurth et al., 2021). I think it is also worth discussing why sex differences can't be found in the evolutionary effect.

Reference:

Hines, M. (2011). Gender development and the human brain. Annual review of neuroscience, 34, 69-88.

Kurth, F., Gaser, C., & Luders, E. (2021). Development of sex differences in the human brain. Cognitive Neuroscience, 12(3-4), 155-162.

It is recommended that the authors explore different prediction models for different species. Maybe macaques are suitable for linear prediction models, and humans are suitable for nonlinear prediction models.

Thank you for pointing the typos out and comments on sex difference. In Figure Supplement 3A, there are typos for Pearson’s r values and we have corrected it in updated Figure 2-figure supplement 3. For details, please see the updated Figure 2-figure supplement 3 and the following figure.

Regarding gender effects, we acknowledge your point about the importance of gender differences in understanding brain evolution and development. In our study, however, our primary goal was to develop a robust age prediction model by maximizing the number of training samples. To mitigate gender-related effects in our main results, we incorporated gender information as a covariate in the ComBat harmonization process. We conducted a supplementary analysis just to demonstrate the stability of our proposed cross-species age prediction model by separating the data with gender variable not to investigate gender differences. Although our results demonstrated that gender-specific models could still significantly predict chronological age, we refrained from emphasizing these models' performance in gender-specific species comparisons due to difficulty in explanation for the predicted gender difference. For cross-species prediction, whether a higher Pearson’s r value between actual age and predicted age could reflect conserved evolution for male or female is not convincing. In addition, we adopted same not different prediction models for human and macaque aiming to establish a comparable model between species. Generally speaking, the nonlinear model could obtain better prediction accuracy than linear model. If different species used different models, it is unfair to perform cross-species prediction. Importantly, our study aimed to developed new index based on the same prediction models to quantify brain evolution difference, i.e., brain cross-species age gap (BCAP) instead of traditional statistical analyses. Different prediction models for different species may introduce bias causing by prediction methods and thus impacting the accuracy of BCAP. Thus, we adopted the linear model with best prediction performances for intra-species prediction in this study for cross-species prediction. Although our main goal in this study is to set up stable cross-species prediction model and the models built using either male or female subjects showed good performances during cross-species prediction, however, as your comment, how to unbiasedly characterize evolutionary gender differences using machining learning approaches needs to be further investigated since there are many reports about the gender difference in developing brain in humans. In fact, whether macaque brains have the same gender differences as humans is an interesting scientific question worth studying. Thus, we have included a discussion on how to use machining learning method to study the evolutionary gender difference in our revised manuscript.

On page 15, lines 18-23 and page 16, line 1-4

“Many studies have reported sex differences in developing human brains (Hines, 2011; Kurth, Gaser, & Luders, 2021), however, whether macaque brains have similar sex differences as humans is still unknown. We used machining learning method for cross-species prediction to quantify brain evolution and the established prediction models are stable even when only using male or female data, which may indicate that the proposed cross-species prediction model has no evolutionary sex difference. Although the stable prediction model can be established in either male or female participants for cross-species prediction, this indeed does not mean that there are no evolutionary sex differences due to lack of quantitative comparative analysis. In the future, we need to develop more objective, quantifiable and stable index for studying sex differences using machining learning methods to further identify sex differences in the evolved brain”

Reviewer #3 (Public Review):

The authors identified a series of WM and GM features that correlated with age in human and macaque structural imaging data. The data was gathered from the HCP and WA studies, which was parcellated in order to yield a set of features. Features that correlated with age were used to train predictive intra and inter-species models of human and macaque age. Interestingly, while each model accurately predicted the corresponding species age, using the macaque model to predict human age was more accurate than the inverse (using the human model to predict macaque age). In addition, the prediction error of the macaque model in predicting human age increased with age, whereas the prediction error of the human model predicting macaque age decreased with age.

After elaboration of the predictive models, the authors classified the features for prediction into human-specific, macaque-specific and common to human and macaque, where they most notably found that macaque-only and common human-macaque areas were located mainly in gray matter, with only a few human-specific features found in gray matter. Furthermore, the authors found significant correlations between BCAP and picture vocabulary (positive correlation) test and visual sensitivity (negative correlation) test. Several white matter tracts (AF, OR, SLFII) were also identified showing a correlation with BCAP.

Thank you for providing this excellent summary. We appreciate your thorough review and concise overview of our work.

STRENGTHS AND WEAKNESSES

The paper brings an interesting perspective on the evolutionary trajectories of human and non-human primate brain structure, and its relation to behavior and cognition. Overall, the methods are robust and support the theoretical background of the paper. However, the overall clarity of the paper could be improved. There are many convoluted sentences and there seems to be both repetition across the different sections and unclear or missing information. For example, the Introduction does not clearly state the research questions, rather just briefly mentions research gaps existing in the literature and follows by describing the experimental method. It would be desirable to clearly state the theoretical background and research questions and leave out details on methodology. In addition, the results section repeats a lot of what is already stated in the methods. This could be further simplified and make the paper much easier to read.

In the discussion, authors mention that "findings about cortex expansion are inconsistent and even contradictory", a more convincing argument could be made by elaborating on why the cortex expansion index is inadequate and how BCAP is more accurate.

Thank you for highlighting the interesting aspects of our work. We are sorry for the lack of the clarity in certain parts of our manuscript. Following your valuable suggestions, we have revised the manuscript to reduce unnecessary repetitions and provide a clearer statement of our research question in Introduction. Specifically, unlike previous analyses of human and macaque evolution using comparative neuroscience, this study embeds chronological axis into the cross-species evolutionary analysis process. It constructed a linear prediction model of brain age for humans and macaques, and quantitatively described the degree of evolution. The brain structure based cross-species age prediction model and cross-species brain age differences proposed in this study further eliminate the inherent developmental effects of humans and macaques on cross-species evolutionary comparisons, providing new perspectives and approaches for studying cross-species development. Regarding the existing repetition in the results section, we have simplified them for the clarity. Regarding the comparison between the cortex expansion index and BCAP, we would like to emphasize that the cortex expansion index was derived without fully considering cross-species alignment along the chronological axis. Specifically, this index does not correspond to a specific developmental stage, but rather focuses on a direct comparison between the two species. In contrast, BCAP addresses this limitation by utilizing a prediction model to establish alignment (or misalignment) between species at the individual level. Therefore, BCAP may serve as a more flexible and nuanced tool for cross-species brain comparison.

STUDY AIMS AND STRENGTH OF CONCLUSIONS

Overall, the methods are robust and support the theoretical background of the paper, but it would be good to state the specific research questions -even if exploratory in nature- more specifically. Nevertheless, the results provide support for the research aims.

Thank you for excellent suggestion. We have revised our introduction to state the specific research question as mentioned above.

IMPACT OF THE WORK AND UTILITY OF METHODS AND DATA TO THE COMMUNITY

This study is a good first step in providing a new insight into the neurodevelopmental trajectories of humans and non-human primates besides the existing cortical expansion theories.

Thank you for your encouraging comment.

ADDITIONAL CONTEXT:

It should be clearly stated both in the abstract and methods that the data used for the experiment came from public databases.

Thank you for your suggestion. We have added this information in both abstract and method. For details, please see page 2, line 9 in Abstract section; page 16, lines 10-11 and page 17, lines 6-10 in Materials and Method section.

Author response:

Reviewer #1 (Public Review):

Using structural analysis, Bonchuk and colleagues demonstrate that the TTK-like BTB/POZs of insects form stable hexameric assemblies composed of trimers of POZ dimers, a configuration observed consistently across both homomultimers and heteromultimers, which are known to be formed by TTK-like BTB/POZ domains. The structural data is comprehensive, unambiguous, and further supported by theoretical fold prediction analyses. In particular the judicious complementation of experiments and fold prediction is commendable. This study now adds an important cog that might help generalize the general principles of the evolution of multimerization in members of this fold family.

I strongly feel that enhancing the inclusivity of the discussion would strengthen the paper. Below, I suggest some additional points for consideration for the same.

Major points.

1) It would be valuable to discuss alternative multimer assembly interfaces, considering the diverse ways POZs can multimerize. For instance, the Potassium channel POZ domains form tetramers. A comparison of their inter-subunit interface with that of TTK and non-TTK POZs could provide insightful contrasts.

Thanks for the suggestion, we added this important comparison, as well as comparison with recently published structures of filament-forming BTB domains.

2) The so-called TTK motif, despite its unique sequence signature, essentially corresponds to the N-terminal extension observed in other "non-TTK" proteins such as Miz-1. Given Miz-1's structure, it becomes evident that the utilization of the N-terminal extension for dimerization is shared with the TTK family, suggesting a common evolutionary origin in metazoan transcription factors. Early phylogenetic trees (e.g. in PMID: 9917379) support the grouping of the TTK-like POZs with other animal Transcription factors containing POZ domains such as those with Kelch repeats further suggesting that the extension might be ancestral. Structural investigations by modeling prominent examples or comparing known structures of similar POZ domains, could support this inference. Control comparisons with POZ domains from fungi, plants and amoebozoans like Dictyostelium could offer additional insights.

We performed AlphaFold2-Multimer modeling of dimers of all BTB domains from the most ancestral metazoan clades, Placozoa and Porifera, along with BTBs from Choanoflagellates – the closest to first metazoans unicellular eukaryotes. The presence of N-terminal beta-sheet was evaluated. KLHL-BTBs are present in all eukaryotes and likely are predecessors of ZBTB domains. According to AlphaFold modeling of dimers, all KLHL-BTB domains of plants and basal metazoans have alpha1 helix, but most of these domains from do not possess additional N-terminal beta-strand (beta1) characteristic for ZBTB domains. We found only one KLHL-BTB (Uniprot ID: AA9VCT1_MONBE) with such N-terminal extension in Choanoflagellate proteome, one in Dictyostelium proteome (Q54F31_DICDI), and 7 (out of 43 BTB domains in total) and 13 (out of 81) such domains in Trichoplax and Amphimedon proteomes correspondingly. There was no significant sequence similarity of beta1 element at the level of primary sequence. However, most of these domains bear 3-box/BACK extension and represent typical KLHL-BTBs which are member of E3 ubiquitin-ligase complexes, they are often associated with protein-protein interacting MATH domain or WD40 repeats. We found only one protein in Trichoplax proteome with beta1 strand devoid of 3-box/BACK (B3RQ74_TRIAD), thus resembling ZBTB topology. Thus, likely emergence of BTB domains of this subtype occurred early in Metazoan evolution. At this point ZBTBs were not yet associated with zinc-fingers. According to our survey, actual fusion of ZBTB domain with zinc-finger domains occurred in the evolution of earlier bilaterian organisms since proteins with such domain architecture are not found in Radiata but are present in basal Protostomia and Deuterostomia clades. TTK-type sequence is characteristic only for Arthropoda and emerged early in their evolution. We added all these data to the article.

3) Exploring the ancestral presence of the aforementioned extension in metazoan transcription factors could serve as a foundation for understanding the evolutionary pathway of hexamerization. This analysis could shed light on exposed structural regions that had the potential to interact post-dimerization with the N-terminal extension and also might provide insights into the evolution of multimer interfaces, as observed in the Potassium channel.

We added this important comparison as well as comparison with recent structures of filament-forming BTB domains.

4) Considering the role of conserved residues in the multimer interface is crucial. Reference to conserved residues involved in multimer formation, such as discussed in PMID: 9917379, would enrich the discussion.

We updated our description of multimer interface with respect to conservation of residues.

Reviewer #2 (Public Review):

BTB domains are protein-protein interaction domains found in diverse eukaryotic proteins, including transcription factors. It was previously known that many of the Drosophila transcription factor BTB domains are of the TTK-type - these are defined as having a highly-conserved motif, FxLRWN, at their N-terminus, and they thereby differ from the mammalian BTB domains. Whereas the well-characterised mammalian BTB domains are dimeric, several Drosophila TTK-BTB domains notably form multimers and function as chromosome architectural proteins. The aims of this work were (i) to determine the structural basis of multimerisation of the Drosophila TTK-BTB domains, (ii) to determine how different Drosophila TTK-BTB domains interact with each other, and (iii) to investigate the evolution of this subtype of BTB domain.

The work significantly advances our understanding of the biology of BTB domains. The conclusions of the paper are mostly well-supported, although some aspects need clarification:

Hexameric organisation of the TTK-type BTB domains:

Using cryo-EM, the authors showed that the CG6765 TTK-type BTB domain forms a hexameric assembly in which three "classic" BTB dimers interact via a beta-sheet interface involving the B3 strand. This is particularly interesting, as this region of the BTB domain has recently been implicated in protein-protein interactions in a mammalian BTB-transcription factor, MIZ1. SEC-MALS analysis indicated that the LOLA TTK-type BTB domain is also hexameric, and SAXS data was consistent with a hexameric assembly of the CG6765- and LOLA BTB domains.

The data regarding the hexameric organisation is convincing. However, interpreting the role of specific regions of the BTB domain is difficult because the description of the molecular contacts lacks depth.

Heteromeric interactions between TTK-type BTB domains:

The authors use yeast two-hybrid assays to study heteromeric interactions between various Drosophila TTK-type BTB domains. Such assays are notorious for producing false positives, and this needs to be mentioned. Although the authors suggest that the heteromeric interactions are mediated via the newly-identify B3 interaction interface, there is no evidence to support this, since mutation of B3 yielded insoluble proteins.

We are aware that Y2H can give false positive results in cases where the BTB domain fused to the DNA binding domain can activate reporter genes. Therefore, all tested BTB domains were examined for their ability to activate transcription. Furthermore, in our study, assays with non-TTK-type BTB domains, which showed almost no interactions, provide additional negative control. We have added a corresponding disclaimer in the text. We agree that our data do not explain the basis for heteromeric interactions. Design of mutations in B3 beta-sheet proved to be complicated, using of biochemical methods to study the principles of heteromer assembly also does not seem to be feasible since most TTK-type BTBs tend to form aggregates and are difficult to be expressed and purified. But most important issue is that demonstrated ability of heteromer assembly through B3 in few tested pairs cannot be applied for all pairs, some of them still may use different mechanism. We used AlphaFold to predict possible mechanisms of heteromer assemblies. AlphaFold suggested that usage of both B3 and conventional dimerization interfaces for heteromeric interactions are possible in various cases, with preference of one over another in different pairs. Thus, most likely the presence of two potential heteromerization interfaces extends the heteromerization capability of these domains. We changed the text accordingly.

Evolution of the TTK-type BTB domains:

The authors carried out a bioinformatics analysis of BTB proteins and showed that most of the Drosophila BTB transcription factors (24 out of 28) are of the TTK-type. They investigated how the TTK-type BTB domains emerged during evolution, and showed that these are only found in Arthropoda, and underwent lineage-specific expansion in the modern phylogenetic groups of insects. These findings are well-supported by the evidence.

Reviewer #2 (Public Review):

BTB domains are protein-protein interaction domains found in diverse eukaryotic proteins, including transcription factors. It was previously known that many of the Drosophila transcription factor BTB domains are of the TTK-type - these are defined as having a highly-conserved motif, FxLRWN, at their N-terminus, and they thereby differ from the mammalian BTB domains. Whereas the well-characterised mammalian BTB domains are dimeric, several Drosophila TTK-BTB domains notably form multimers and function as chromosome architectural proteins. The aims of this work were (i) to determine the structural basis of multimerisation of the Drosophila TTK-BTB domains, (ii) to determine how different Drosophila TTK-BTB domains interact with each other, and (iii) to investigate the evolution of this subtype of BTB domain.

The work significantly advances our understanding of the biology of BTB domains. The conclusions of the paper are mostly well-supported, although some aspects need clarification:

Hexameric organisation of the TTK-type BTB domains:<br /> Using cryo-EM, the authors showed that the CG6765 TTK-type BTB domain forms a hexameric assembly in which three "classic" BTB dimers interact via a beta-sheet interface involving the B3 strand. This is particularly interesting, as this region of the BTB domain has recently been implicated in protein-protein interactions in a mammalian BTB-transcription factor, MIZ1. SEC-MALS analysis indicated that the LOLA TTK-type BTB domain is also hexameric, and SAXS data was consistent with a hexameric assembly of the CG6765- and LOLA BTB domains.

The data regarding the hexameric organisation is convincing. However, interpreting the role of specific regions of the BTB domain is difficult because the description of the molecular contacts lacks depth.

Heteromeric interactions between TTK-type BTB domains:<br /> The authors use yeast two-hybrid assays to study heteromeric interactions between various Drosophila TTK-type BTB domains. Such assays are notorious for producing false positives, and this needs to be mentioned. Although the authors suggest that the heteromeric interactions are mediated via the newly-identify B3 interaction interface, there is no evidence to support this, since mutation of B3 yielded insoluble proteins.

Evolution of the TTK-type BTB domains:<br /> The authors carried out a bioinformatics analysis of BTB proteins and showed that most of the Drosophila BTB transcription factors (24 out of 28) are of the TTK-type. They investigated how the TTK-type BTB domains emerged during evolution, and showed that these are only found in Arthropoda, and underwent lineage-specific expansion in the modern phylogenetic groups of insects. These findings are well-supported by the evidence.

Author response:

Reviewer #1 - Public Review

This report describes work aiming to delineate multi-modal MRI correlates of psychopathology from a large cohort of children of 9-11 years from the ABCD cohort. While uni-modal characterisations have been made, the authors rightly argue that multi-modal approaches in imaging are vital to comprehensively and robustly capture modes of large-scale brain variation that may be associated with pathology. The primary analysis integrates structural and resting-state functional data, while post-hoc analyses on subsamples incorporate task and diffusion data. Five latent components (LCs) are identified, with the first three, corresponding to p-factor, internal/externalising, and neurodevelopmental Michelini Factors, described in detail. In addition, associations of these components with primary and secondary RSFC functional gradients were identified, and LCs were validated in a replication sample via assessment of correlations of loadings.

1.1) This work is clearly novel and a comprehensive study of associations within this dataset. Multi-modal analyses are challenging to perform, but this work is methodologically rigorous, with careful implementation of discovery and replication assessments, and primary and exploratory analyses. The ABCD dataset is large, and behavioural and MRI protocols seem appropriate and extensive enough for this study. The study lays out comprehensive associations between MRI brain measures and behaviour that appear to recapitulate the established hierarchical structure of psychopathology.

We thank Reviewer 1 for appreciating our methods and findings, and we address their suggestions below:

1.2) The work does have weaknesses, some of them acknowledged. There is limited focus on the strength of observed associations. While the latent component loadings seem reliably reproducible in the behavourial domain, this is considerably less the case in the imaging modalities. A considerable proportion of statistical results focuses on spatial associations in loadings between modalities - it seems likely that these reflect intrinsic correlations between modalities, rather than associations specific to any latent component.

We appreciate the Reviewer’s comment, and minimized the reporting of correlations between the loadings from the different modalities in the revised Results (specifically subsections on LC1, LC2, and LC3). We now refer to Table S4 in each subsection for this information: “Spatial correlations between modality-specific loadings are reported in Supplementary file 1c.”

For completeness, we report the intrinsic correlations between the different modalities in Supplementary file 1c (P.19):

“Lastly, although the current work aimed to reduce intrinsic correlations between variables within a given modality through running a PCA before the PLS approach, intrinsic correlations between measures and modalities may potentially be a remaining factor influencing the PLS solution. We, thus, provided an additional overview of the intrinsic correlations between the different neuroimaging data modalities in the supporting results (Supplementary file 1c).”

1.3) Assessment of associations with functional gradients is similarly a little hard to interpret. Thus, it is hard to judge the implications for our understanding of the neurophysiological basis of psychopathology and the ability of MRI to provide clinical tools for, say, stratification.

We now provide additional context, including a rising body of theoretical and empirical work, that outlines the value of functional gradients and cortical hierarchies in the understanding of brain development and psychopathology. Please see P.26.

“Initially demonstrated at the level of intrinsic functional connectivity (Margulies et al., 2016), follow up work confirmed a similar cortical patterning using microarchitectural in-vivo MRI indices related to cortical myelination (Burt et al., 2018; Huntenburg et al., 2017; Paquola et al., 2019), post-mortem cytoarchitecture (Goulas et al., 2018; Paquola et al., 2020, 2019), or post-mortem microarray gene expression (Burt et al., 2018). Spatiotemporal patterns in the formation and maturation of large-scale networks have been found to follow a similar sensory-to-association axis; moreover, there is the emerging view that this framework may offer key insights into brain plasticity and susceptibility to psychopathology (Sydnor et al., 2021). In particular, the increased vulnerability of transmodal association cortices in late childhood and early adolescence has been suggested to relate to prolonged maturation and potential for plastic reconfigurations of these systems (Paquola et al., 2019; Park et al., 2022b). Between mid-childhood and early adolescence, heteromodal association systems such as the default network become progressively more integrated among distant regions, while being more differentiated from spatially adjacent systems, paralleling the development of cognitive control, as well as increasingly abstract and logical thinking. [...] This suggests that neurodevelopmental difficulties might be related to alterations in various processes underpinned by sensory and association regions, as well as the macroscale balance and hierarchy of these systems, in line with previous findings in several neurodevelopmental conditions, including autism, schizophrenia, as well as epilepsy, showing a decreased differentiation between the two anchors of this gradient (Hong et al., 2019). In future work, it will be important to evaluate these tools for diagnostics and population stratification. In particular, the compact and low dimensional perspective of gradients may provide beneficial in terms of biomarker reliability as well as phenotypic prediction, as previously demonstrated using typically developing cohorts (Hong et al. 2020) On the other hand, it will be of interest to explore in how far alterations in connectivity along sensory-to-transmodal hierarchies provide sufficient graduality to differentiate between specific psychopathologies, or whether they, as the current work suggests, mainly reflect risk for general psychopathology and atypical development.”

1.4) The observation of a recapitulation of psychopathology hierarchy may be somewhat undermined by the relatively modest strength of the components in the imaging domain.

We thank the Reviewer for this comment, and now expressed this limitation in the revised Discussion, P.23.

“The p factor, internalizing, externalizing, and neurodevelopmental dimensions were each associated with distinct morphological and intrinsic functional connectivity signatures, although these relationships varied in strength.”

1.5) The task fMRI was assessed with a fairly basic functional connectivity approach, not using task timings to more specifically extract network responses.

In the revised Discussion on P.24, we acknowledge that more in-depth analyses of task-based fMRI may have offered additional insights into state-dependent changes in functional architecture.

“While the current work derived main imaging signatures from resting-state fMRI as well as grey matter morphometry, we could nevertheless demonstrate associations to white matter architecture (derived from diffusion MRI tractography) and recover similar dimensions when using task-based fMRI connectivity. Despite subtle variations in the strength of observed associations, the latter finding provided additional support that the different behavioral dimensions of psychopathology more generally relate to alterations in functional connectivity. Given that task-based fMRI data offers numerous avenues for analytical exploration, our findings may motivate follow-up work assessing associations to network- and gradient-based response strength and timing with respect to external stimuli across different functional states.”

1.6) Overall, the authors achieve their aim to provide a detailed multimodal characterisation of MRI correlations of psychopathology. Code and data are available and well organised and should provide a valuable resource for researchers wanting to understand MRI-based neural correlates of psycho-pathology-related behavioural traits in this important age group. It is largely a descriptive study, with comparisons to previous uni-modal work, but without particularly strong testing of neuroscience hypotheses.

We thank the Reviewer for recognizing the detail and rigor of data-driven study and extensive code and data documentation.

Reviewer #2 - Public Review

In "Multi-modal Neural Correlates of Childhood Psychopathology" Krebets et al. integrate multi-modal neuroimaging data using machine learning to delineate dissociable links to diverse dimensions of psychopathology in the ABCD sample. This paper had numerous strengths including a superb use of a large resource dataset, appropriate analyses, beautiful visualizations, clear writing, and highly interpretable results from a data-driven analysis. Overall, I think it would certainly be of interest to a general readership. That being said, I do have several comments for the authors to consider.

We thank Dr Satterthwaite for the positive evaluation and helpful comments.

2.1) Out-of-sample testing: while the permutation testing procedure for the PLS is entirely appropriate, without out-of-sample testing the reported effect sizes are likely inflated.

As discussed in the editorial summary of essential revisions, we agree that out-of-sample prediction indeed provides stronger estimates of generalizability. We assess this by applying the PCA coefficients derived from the discovery cohort imaging data to the replication cohort imaging data. The resulting PCA scores and behavioral data were then z-scored using the mean and standard deviation of the replication cohort. The SVD weights derived from the discovery cohort were applied to the normalized replication cohort data to derive imaging and behavioral composite scores, which were used to recover the contribution of each imaging and behavioral variable to the LCs (i.e., loadings). Out-of-sample replicability of imaging (mean r=0.681, S.D.=0.131) and behavioral (mean r=0.948, S.D.=0.022) loadings was generally high across LCs 1-5. This analysis is reported in the revised manuscript (P.18).

“Generalizability of reported findings was also assessed by directly applying PCA coefficients and latent components weights from the PLS analysis performed in the discovery cohort to the replication sample data. Out-of-sample prediction was overall high across LCs1-5 for both imaging (mean r=0.681, S.D.=0.131) and behavioral (mean r=0.948, S.D.=0.022) loadings.”

2.2) Site/family structure: it was unclear how site/family structure were handled as covariates.

Only unrelated participants were included in discovery and replication samples (see P.6). The site variable was regressed out of the imaging and behavioral data prior to the PLS analysis using the residuals from a multiple linear model which also included age, age2, sex, and ethnicity. This is now clarified on P.29:

“Prior to the PLS analysis, effects of age, age2, sex, site, and ethnicity were regressed out from the behavioral and imaging data using a multiple linear regression to ensure that the LCs would not be driven by possible confounders (Kebets et al., 2021, 2019; Xia et al., 2018). The imaging and behavioral residuals of this procedure were input to the PLS analysis.”

2.3) Anatomical features: I was a bit surprised to see volume, surface area, and thickness all evaluated - and that there were several comments on the correspondence between the SA and volume in the results section. Given that cortical volume is simply a product of SA and CT (and mainly driven by SA), this result may be pre-required.

As suggested, we reduced the reporting of correlations between the loadings from the different modalities in the revised Results (specifically subsections on LC1, LC2, and LC3). Instead, we now refer to Table S4 in each subsection for this information: “Spatial correlations between modality-specific loadings are reported in Supplementary file 1c.”

We also reran the PLS analysis while only including thickness and surface area as our structural metrics, to account for potential redundancy of these measures with volume. This analysis and associated findings are reported on P.36 and P.19:

“As cortical volume is a result of both thickness and surface area, we repeated our main PLS analysis while excluding cortical volume from our imaging metrics and report the consistency of these findings with our main model.”

“Third, to account for redundancy within structural imaging metrics included in our main PLS model (i.e., cortical volume is a result of both thickness and surface area), we also repeated our main analysis while excluding cortical volume from our imaging metrics. Findings were very similar to those in our main analysis, with an average absolute correlation of 0.898±0.114 across imaging composite scores of LCs 1-5.”

2.4) Ethnicity: the rationale for regressing ethnicity from the data was unclear and may conflict with current best practices.

We thank the Reviewer for this comment. In light of recent discussions on including this covariate in large datasets such as ABCD (e.g., Saragosa-Harris et al., 2022), we elaborate on our rationale for including this variable in our model in the revised manuscript on P.30:

“Of note, the inclusion of ethnicity as a covariate in imaging studies has been recently called into question. In the present study, we included this variable in our main model as a proxy for social inequalities relating to race and ethnicity alongside biological factors (age, sex) with documented effects on brain organization and neurodevelopmental symptomatology queried in the CBCL.”

We also assess the replicability of our analyses when removing race and ethnicity covariates prior to computing the PLS analysis and correlating imaging and behavioral composite scores across both models. We report resulting correlations in the revised manuscript (P.37, 19, and 27):

“We also assessed the replicability of our findings when removing race and ethnicity covariates prior to computing the PLS analysis and correlating imaging and behavioral composite scores across both models.”

“Moreover, repeating the PLS analysis while excluding this variable as a model covariate yielded overall similar imaging and behavioral composites scores across LCs to our original analysis. Across LCs 1-5, the average absolute correlations reached r=0.636±0.248 for imaging composite scores, and r=0.715±0.269 for behavioral composite scores. Removing these covariates seemed to exert stronger effects on LC3 and LC4 for both imaging and behavior, as lower correlations across models were specifically observed for these components.”

“Although we could consider some socio-demographic variables and proxies of social inequalities relating to race and ethnicity as covariates in our main model, the relationship of these social factors to structural and functional brain phenotypes remains to be established with more targeted analyses.”

2.5) Data quality: the authors did an admirable job in controlling for data quality in the analyses of functional connectivity data. However, it is unclear if a comparable measure of data quality was used for the T1/dMRI analyses. This likely will result in inflated effect sizes in some cases; it has the potential to reduce sensitivity to real effects.

We agree that data quality was not accounted for in our analysis of T1w- and diffusion-derived metrics. We now accounted for T1w image quality by adding manual quality control ratings to the regressors applied to all structural imaging metrics prior to performing the PLS analysis, and reported the consistency of this new model with original findings. See P.36, P.19:

“We also considered manual quality control ratings as a measure of T1w scan quality. This metric was included as a covariate in a multiple linear regression model accounting for potential confounds in the structural imaging data, in addition to age, age2, sex, site, ethnicity, ICV, and total surface area. Downstream PLS results were then benchmarked against those obtained from our main model.”

“Considering scan quality in T1w-derived metrics (from manual quality control ratings) yielded similar results to our main analysis, with an average correlation of 0.986±0.014 across imaging composite scores.”

As for diffusion imaging, we also regressed out effects of head motion in addition to age, age2, sex, site, and ethnicity from FA and MD measures and reported the consistency with our original results (P.36, P.19):

“We tested another model which additionally included head motion parameters as regressors in our analyses of FA and MD measures, and assessed the consistency of findings from both models.”

“Additionally considering head motion parameters from diffusion imaging metrics in our model yielded consistent results to those in our main analyses (mean r=0.891, S.D.=0.103; r=0.733-0.998).”

Reviewer #3 - Public Review

In this study, the authors utilized the Adolescent Brain Cognitive Development dataset to investigate the relationship between structural and functional brain network patterns and dimensions of psychopathology. They identified multiple components, including a general psychopathology (p) factor that exhibited a strong association with multimodal imaging features. The connectivity signatures associated with the p factor and neurodevelopmental dimensions aligned with the sensory-to-transmodal axis of cortical organization, which is linked to complex cognition and psychopathology risk. The findings were consistent across two separate subsamples and remained robust when accounting for variations in analytical parameters, thus contributing to a better understanding of the biological mechanisms underlying psychopathology dimensions and offering potential brain-based vulnerability markers.

3.1) An intriguing aspect of this study is the integration of multiple neuroimaging modalities, combining structural and functional measures, to comprehensively assess the covariance with various symptom combinations. This approach provides a multidimensional understanding of the risk patterns associated with mental illness development.

We thank the Reviewer for acknowledging the multimodal approach, and for the constructive suggestions.

3.2) The paper delves deeper into established behavioral latent variables such as the p factor, internalizing, externalizing, and neurodevelopmental dimensions, revealing their distinct associations with morphological and intrinsic functional connectivity signatures. This sheds light on the neurobiological underpinnings of these dimensions.

We are happy to hear the Reviewer appreciates the gain in understanding neural underpinnings of dimensions of psychopathology resulting from the current work.

3.3) The robustness of the findings is a notable strength, as they were validated in a separate replication sample and remained consistent even when accounting for different parameter variations in the analysis methodology. This reinforces the generalizability and reliability of the results.

We appreciate that the Reviewer found our robustness and generalizability assessment convincing.

3.4) Based on their findings, the authors suggest that the observed variations in resting-state functional connectivity may indicate shared neurobiological substrates specific to certain symptoms. However, it should be noted that differences in resting-state connectivity between groups can stem from various factors, as highlighted in the existing literature. For instance, discrepancies in the interpretation of instructions during the resting state scan can influence the results. Hence, while their findings may indicate biological distinctions, they could also reflect differences in behavior.

For the ABCD dataset, resting-state fMRI scans were based on eyes open and passive viewing of a crosshair, and are thus homogenized. We acknowledge, however, that there may still be state-to-state fluctuations contributing to the findings, and this is now discussed in the revised Discussion, on P.28. Note, however, that prior literature has generally also suggested rather modest impacts of cognitive and daily variation on resting-state functional networks, compared to much more dominating inter-individual and inter-group factors.

“Finally, while prior research has shown that resting-state fMRI networks may be affected by differences in instructions and study paradigm (e.g., with respect to eyes open vs closed) (Agcaoglu et al., 2019), the resting-state fMRI paradigm is homogenized in the ABCD study to be passive viewing of a centrally presented fixation cross. It is nevertheless possible that there were slight variations in compliance and instructions that contributed to differences in associated functional architecture. Notably, however, there is a mounting literature based on high-definition fMRI acquisitions suggesting that functional networks are mainly dominated by common organizational principles and stable individual features, with substantially more modest contributions from task-state variability (Gratton et al. 2018). These findings, thus, suggest that resting-state fMRI markers can serve as powerful phenotypes of psychiatric conditions, and potential biomarkers (Abraham et al., 2017; Gratton et al., 2020; Parkes et al., 2020).”

3.5) The authors conducted several analyses to investigate the relationship between imaging loadings associated with latent components and the principal functional gradient. They found several associations between principal gradient scores and both within- and between-network resting-state functional connectivity (RSFC) loadings. Assessing the analysis presented here proves challenging due to the nature of relating loadings, which are partly based on the RSFC, to gradients derived from RSFC. Consequently, a certain level of correlation between these two variables would be expected, making it difficult to determine the significance of the authors' findings. It would be more intriguing if a direct correlation between the composite scores reflecting behavior and the gradients were to yield statistically significant results.

We thank the Reviewer for the comment, and agree that investigating gradient-behavior relationships could offer additional insights into the neural basis of psychiatric symptomatology. However, the current analysis pipeline precludes this direct comparison which is performed on a region-by-region basis across the span of the cortical gradient. Indeed, the behavioral loadings are provided for each CBCL item, and not cortical regions.

The Reviewer also evokes concerns of potential circularity in our analysis, as we compared imaging loadings, which are partially based on RSFC, and gradient values generated from the same RSFC data. In response to this comment, we cross-validated our findings using an RSFC gradient derived from an independent dataset (HCP), showing highly consistent findings to those presented in the manuscript. This correlation is now reported in the Results section P.15.

“A similar pattern of findings was observed when cross-validating between- and within-network RSFC loadings to a RSFC gradient derived from an independent dataset (HCP), with strongest correlations seen for between-network RSFC loadings for LC1 and LC3 (LC1: r=0.50, pspin<0.001; LC3: r=0.37, pspin<0.001).”

We furthermore note similar correlations between imaging loadings and T1w/T2w ratio in the same participants, a proxy of intracortical microstructure and hierarchy (Glasser et al., 2011). These findings are now detailed in the revised Results, P.15-16:

“Of note, we obtain similar correlations when using T1w/T2w ratio in the same participants, a proxy of intracortical microstructure and hierarchy (Glasser et al., 2011). Specifically, we observed the strongest association between this microstructural marker of the cortical hierarchy and between-network RSFC loadings related to LC1 (r=-0.43, pspin<0.001).”

3.6) Lastly, regarding the interpretation of the first identified latent component, I have some reservations. Upon examining the loadings, it appears that LC1 primarily reflects impulse control issues rather than representing a comprehensive p-factor. Furthermore, it is worth noting that within the field, there is an ongoing debate concerning the interpretation and utilization of the p-factor. An insightful publication on this topic is "The p factor is the sum of its parts, for now" (Fried et al, 2021), which explains that the p-factor emerges as a result of a positive manifold, but it does not necessarily provide insights into the underlying mechanisms that generated the data.

We thank the Reviewer for this comment, and added greater nuance into the discussion of the association to the p factor. We furthermore discuss some of the ongoing debate about the use of the p factor, and cite the recommended publication on P.27.

“Other factors have also been suggested to impact the development of psychopathology, such as executive functioning deficits, earlier pubertal timing, negative life events (Brieant et al., 2021), maternal depression, or psychological factors (e.g., low effortful control, high neuroticism, negative affectivity). Inclusion of such data could also help to add further mechanistic insights into the rather synoptic proxy measure of the p factor itself (Fried et al., 2021), and to potentially assess shared and unique effects of the p factor vis-à-vis highly correlated measures of impulse control.”

Author response:

Reviewer #2 (Public Review):

This is, to my knowledge, the most scalable method for phylogenetic placement that uses likelihoods. The tool has an inter- esting and innovative means of using gaps, which I haven’t seen before. In the validation the authors demonstrate superior performance to existing tools for taxonomic annotation (though there are questions about the setup of the validation as described below).

The program is written in C with no library dependencies. This is great. However, I wasn’t able to try out the software because the linking failed on Debian 11, and the binary artifact made by the GitHub Actions pipeline was too recent for my GLIBC/kernel. It’d be nice to provide a binary for people stuck on older kernels (our cluster is still on Ubuntu 18.04). Also, would it be hard to publish your .zipped binaries as packages?

We have provided a binary (and zipped package) that supports Ubuntu 18.04 in GitHub Actions ( https://github.com/lpipes/tronko/actions/runs/9947708087). This should facilitate the use of our software on older sys- tems like yours. We were not able to test the binary however, since GitHub did not seem to find any nodes with Ubuntu 18.04. It is important to note that Ubuntu 18.04 is deprecated. The latest version of Ubuntu is 24.04, and we recommend users to upgrade to newer, supported versions of their operating systems to benefit from the latest security updates and features.

Thank you for publishing your source files for the validation on zenodo. Please provide a script that would enable the user to rerun the analysis using those files, either on zenodo or on GitHub somewhere.

We have posted all datasets as well as scripts to Zenodo.

The validations need further attention as follows.

First, the authors have not chosen data sets that are not well-aligned with real-world use cases for this software, and as a re- sult, its applicability is difficult to determine. First, the leave-one-species-out experiment made use of COI gene sequences representing 253 species from the order Charadriiformes, which includes bird species such as gulls and terns. What is the reasoning for selecting this data set given the objective of demonstrating the utility of Tronko for large scale community profiling experiments which by their nature tend to include microorganisms as subjects? If the authors are interested in evaluating COI (or another gene target) as a marker for characterizing the composition of eukaryotic populations, is the heterogeneity and species distribution of bird species within order Charadriiformes comparable to what one would expect in populations of organisms that might actually be the target of a metagenomic analysis?

Our reasoning for selecting Charadriiformes is that these species are often misidentified for each other and there is a heavy reliance on COI for their species identification. This choice allows us to demonstrate Tronko’s ability to handle difficult and realistic identification challenges. Additionally, we aimed to simulate a challenging dataset to effectively differentiate between the methods used, showcasing Tronko’s robustness. Including more distantly related bird species would have simplified the identification process, which would not serve our objective of demonstrating the utility of Tronko for dis- tinguishing closely related species. It is also important to note that all methods used the exact same reference database which is not always the case in other species assignment comparative studies.

Furthermore, while our study uses bird species, the principles and techniques applied are broadly applicable to other taxa, including microorganisms. By selecting a datase tknown for its identification difficulties, we underscore Tronko’spotential utility in a wide range of taxonomic profiling scenarios, including those involving high heterogeneity and closely related species, such as in microbial communities.

Second, It appears that experiments evaluating performance for 16S were limited to reclassification of sequencing data from mock communities described in two publications, Schirmer (2015, 49 bacteria and 10 archaea, all environmental), and Gohl (2016; 20 bacteria - this is the widely used commercial mock community from BEI, all well-known human pathogens or commensals). The authors performed a comparison with kraken2, metaphlan2, and MEGAN using both the default database for each as well as the same database used for Tronko (kudos for including the latter). This pair of experiments provide a reasonable high-level indication of Tronko’s performance relative to other tools, but the total number of organ- isms is very limited, and particularly limited with respect to the human microbiome. It is also important to point out that these mock communities are composed primarily of type strains and provide limited species-level heterogeneity. The per- formance of these classification tools on type strains may not be representative of what one would find in natural samples. Thus, the leave-one-individual-out and leave-one-species-out experiments would have been more useful and informative had they been applied to extended 16S data sets representing more ecologically realistic populations.

We thank the reviewer for this comment and we have included both an additional bacterial mock community dataset from Lluch et al. (2015) and an additional leave-one-species-out experiment. We describe how this leave-one-species-out dataset was constructed in our previous response to ’Essential Revisions’ #1. We also added Figure 5, S5, and S6.

Finally, the authors should describe the composition of the databases used for classification as well as the strategy (and toolchain) used to select reference sequences. What databases were the reference sequences drawn from and by what criteria? Were the reference databases designed to reflect the composition of the mock communities (and if so, are they limited to species in those communities, or are additional related species included), or have the authors constructed general pur- pose reference databases? How many representatives of each species were included (on average), and were there efforts to represent a diversity of strains for each species? The methods should include a section detailing the construction of the data sets: as illustrated in this very study, the choice of reference database influences the quality of classification results, and the authors should explain the process and design considerations for database construction.

To construct our databases, we used CRUX (Curd et al., 2018). This is described in the Methods section under ’Custom 16S and COI Tronko-build reference database construction’. All missing outs tests were downsamples of these two databases. It is beyond the scope of the manuscript to discuss how CRUX works. Additionally, we added the following text:

To compare the new method (Tronko) to previous methods, we constructed reference databases for COI and 16S for com- mon amplicon primer sets using CRUX (See Methods for exact primers used).

Author response:

Reviewer #1 (Public Review):

In this manuscript, Perez-Lopez et al. examine the function of the chemokine CCL28, which is expressed highly in mucosal tissues during infection, but its role during infection is poorly understood. They find that CCL28 promotes neutrophil accumulation in the intestines of mice infected with Salmonella and in the lungs of mice infected with Acinetobacter. They find that Ccl28-/- mice are highly susceptible to Salmonella infection, and highly resistant and protected from lethality following Acinetobacter infection. They find that neutrophils express the CCL28 receptors CCR3 and CCR10. CCR3 was pre-formed and intracellular and translocated to the cell surface following phagocytosis or inflammatory stimuli. They also find that CCL28 stimulation of CCR3 promoted neutrophil antimicrobial activity, ROS production, and NET formation, using a combination of primary mouse and human neutrophils for their studies. Overall, the authors' findings provide new and fundamental insight into the role of the CCL28:CCR3 chemokine:chemokine receptor pair in regulating neutrophil recruitment and effector function during infection with the intestinal pathogen Salmonella Typhimurium and the lung pathogen Acinetobacter baumanii.

We would like to thank the reviewer for their positive assessment of our work and for providing us with constructive comments that have helped us to improve the manuscript.

Reviewer #2 (Public Review):

In this manuscript by Perez-Lopez et al., the authors investigate the role of the chemokine CCL28 during bacterial infections in mucosal tissues. This is a well-written study with exciting results. They show a role for CCL28 in promoting neutrophil accumulation to the guts of Salmonella-infected mice and to the lung of mice infected with Acinetobacter. Interestingly, the functional consequences of CCL28 deficiency differ between infections with the two different pathogens, with CCL28-deficiency increasing susceptibility to Salmonella, but increasing resistance to Acinetobacter. The underlying mechanistic reasons for this suggest roles for CCL28 in enhanced neutrophil antimicrobial activity, production of reactive oxygen species, and formation of extracellular traps. However, additional experiments are required to shore up these mechanisms, including addressing the role of other CCL28-dependent cell types and further characterization of neutrophils from CCL28-deficient mice.

We would like to thank the reviewer for the positive assessment of our work and for providing us with constructive comments that have helped us to improve the manuscript.

Reviewer #3 (Public Review):

The manuscript by Perez-Lopez and colleagues uses a combination of in vivo studies using knockout mice and elegant in vitro studies to explore the role of the chemokine CCL28 during bacterial infection on mucosal surfaces. Using the streptomycin model of Salmonella Typhimurium (S. Tm) infection, the authors demonstrate that CCL28 is required for neutrophil influx in the intestinal mucosa to control pathogen burden both locally and systemically. Interestingly, CCL28 plays the opposite role in a model lung infection by Acinetobacter baumanii, as Ccl28-/- mice are protected from Acinetobacter infection. Authors suggest that the mechanism by which CCL28 plays a role during bacterial infection is due to its role in modulating neutrophil recruitment and function.

We would like to thank the reviewer for the positive assessment of our work and for providing us with constructive comments that have helped us to improve the manuscript.

The major strengths of the manuscript are:

The novelty of the findings that are described in the manuscript. The role of the chemokine CCL28 in modulating neutrophil function and recruitment in mucosal surfaces is intriguing and novel.

Authors use Ccl28-/- mice in their studies, a mouse strain that has only recently been available. To assess the impact of CCL28 on mucosal surfaces during pathogen-induced inflammation, the authors choose not one but two models of bacterial infection (S. Tm and A. baumanii). This approach increases the rigor and impact of the data presented.

Authors combine the elegant in vivo studies using Ccl28 -/- with in vitro experiments that explore the mechanisms by which CCL28 affects neutrophil function.

The major weaknesses of the manuscript in its present form are:

Authors use different time points in the S. Tm model to characterize the influx of immune cells and pathology. They do not provide a clear justification as to why distinct time points were chosen for their analysis.

The reviewer raises a good point. As discussed in the detailed response to the reviewers, we have now generated extensive results at different time points and included these in the revised manuscript.

Authors provide puzzling data that Ccl28-/- mice have the same numbers of CCR3 and CCR10- expressing neutrophils in the mucosa during infection. It is unclear why the lack of CCL28 expression would not affect the recruitment of neutrophils that express the ligands (CCR3 and CCR10) for this chemokine. Thus, these results need to be better explained.

As discussed in the detailed response to the reviewers, we clarified that Ccl28-/- mice have reduced numbers of neutrophils in the mucosa during infection, but the percentage of CCR3+ and CCR10+ neutrophils does not change. We provide additional discussion of this point in the manuscript and in the response to the reviewers.

The in vitro studies focus primarily on characterizing how CCL28 affects the function of neutrophils in response to S. Tm infection. There is a lack of data to demonstrate whether Acinetobacter affects CCR3 and CCR10 expression and recruitment to the cell surface and whether CCL28 plays any role in this process.

We agree and have performed additional studies with Acinetobacter and CCL28, which we discuss in greater detail below in the response to the reviewers.

eLife assessment

This is a useful study on sex differences in gene expression across organs of four mice taxa, although there are some shortcomings in the data analyses and interpretations that should to be better placed in the broader context of the current literature. Hence, the evidence in the current form is incomplete, with several overstated key conclusions.

Reviewer #1 (Public Review):

The authors describe a comprehensive analysis of sex-biased expression across multiple tissues and species of mouse. Their results are broadly consistent with previous work, and their methods are robust, as the large volume of work in this area has converged toward a standardized approach.

I have a few quibbles with the findings, and the main novelty here is the rapid evolution of sex-biased expression over shorter evolutionary intervals than previously documented, although this is not statistically supported. The other main findings, detailed below, are somewhat overstated.

(1) In the introduction, the authors conflate gametic sex, which is indeed largely binary (with small sperm, large eggs, no intermediate gametic form, and no overlap in size) with somatic sexual dimorphism, which can be bimodal (though sometimes is even more complicated), with a large variance in either sex and generally with a great deal of overlap between males and females. A good appraisal of this distinction is at https://doi.org/10.1093/icb/icad113. This distinction in gene expression has been recognized for at least 20 years, with observations that sex-biased expression in the soma is far less than in the gonad.

For example, the authors frame their work with the following statement:<br /> "The different organs show a large individual variation in sex-biased gene expression, making it impossible to classify individuals in simple binary terms. Hence, the seemingly strong conservation of binary sex-states does not find an equivalent underpinning when one looks at the gene-expression makeup of the sexes"

The authors use this conflation to set up a straw man argument, perhaps in part due to recent political discussions on this topic. They seem to be implying one of two things. a) That previous studies of sex-biased expression of the soma claim a binary classification. I know of no such claim, and many have clearly shown quite the opposite, particularly studies of intra-sexual variation, which are common - see https://doi.org/10.1093/molbev/msx293, https://doi.org/10.1371/journal.pgen.1003697, https://doi.org/10.1111/mec.14408, https://doi.org/10.1111/mec.13919, https://doi.org/10.1111/j.1558-5646.2010.01106.x for just a few examples. Or b) They are the first to observe this non-binary pattern for the soma, but again, many have observed this. For example, many have noted that reproductive or gonad transcriptome data cluster first by sex, but somatic tissue clusters first by species or tissue, then by sex (https://doi.org/10.1073/pnas.1501339112, https://doi.org/10.7554/eLife.67485)<br /> Figure 4 illustrates the conceptual difference between bimodal and binary sexual conceptions. This figure makes it clear that males and females have different means, but in all cases the distributions are bimodal.

I would suggest that the authors heavily revise the paper with this more nuanced understanding of the literature and sex differences in their paper, and place their findings in the context of previous work.

(2) The authors also claim that "sexual conflict is one of the major drivers of evolutionary divergence already at the early species divergence level." However, making the connection between sex-biased genes and sexual conflict remains fraught. Although it is tempting to use sex-biased gene expression (or any form of phenotypic dimorphism) as an indicator of sexual conflict, resolved or not, as many have pointed out, one needs measures of sex-specific selection, ideally fitness, to make this case (https://doi.org/10.1086/595841, 10.1101/cshperspect.a017632). In many cases, sexual dimorphism can arise in one sex only without conflict (e.g. 10.1098/rspb.2010.2220). As such, sex-biased genes alone are not sufficient to discriminate between ongoing and resolved conflict.

(3) To make the case that sex-biased genes are under selection, the authors report alpha values in Figure 3B. Alpha value comparisons like this over large numbers of genes often have high variance. Are any of the values for male- female- and un-biased genes significantly different from one another? This is needed to make the claim of positive selection.

Reviewer #2 (Public Review):

The manuscript by Xie and colleagues presents transcriptomic experiments that measure gene expression in eight different tissues taken from adult female and male mice from four species. These data are used to make inferences regarding the evolution of sex-biased gene expression across these taxa. The experimental methods and data analysis are appropriate; however, most of the conclusions drawn in the manuscript have either been previously reported in the literature or are not fully supported by the data.

There are two ways the manuscript could be modified to better strengthen the conclusions.

First, some of the observed differences in gene expression have very little to no effect on other phenotypes, and are not relevant to medicine or fitness. Selectively neutral gene expression differences have been inferred in previous studies, and consistent with that work, sex-biased and between-species expression differences in this study may also be enriched for selectively neutral expression differences. This idea is supported by the analysis of expression variance, which indicates that genes that show sex-biased expression also tend to show more inter-individual variation. This perspective is also supported by the MK analysis of molecular evolution, which suggests that positive selection is more prevalent among genes that are sex-biased in both mus and dom, and genes that switch sex-biased expression are under less selection at the level of both protein-coding sequence and gene expression.

As an aside, I was confused by (line 176): "implying that the enhanced positive selection pressure is triggered by their status of being sex-biased in either taxon." - don't the MK values suggest an excess of positive selection on genes that are sex-biased in both taxa?

Without an estimate of the proportion of differentially expressed genes that might be relevant for broader physiological or organismal phenotypes, it is difficult to assess the accuracy and relevance of the manuscript's conclusions. One (crude) approach would be to analyze subsets of genes stratified by the magnitude of expression differences; while there is a weak relationship between expression differences and fitness effects, on average large gene expression differences are more likely to affect additional phenotypes than small expression differences. Another perspective would be to compare the within-species variance to the between-species variance to identify genes with an excess of the latter relative to the former (similar logic to an MK test of amino acid substitutions).

Second, the analysis could be more informative if it distinguished between genes that are expressed across multiple tissues in both sexes that may show greater expression in one sex than the other, versus genes with specialized function expressed solely in (usually) reproductive tissues of one sex (e.g. ovary-specific genes). One approach to quantify this distinction would be metrics like those used defined by [Yanai I, et al. 2005. Genome-wide midrange transcription profiles reveal expression-level relationships in human tissue specification. Bioinformatics 21:650-659.] These approaches can be used to separate out groups of genes by the extent to which they are expressed in both sexes versus genes that are primarily expressed in sex-specific tissue such as testes or ovaries. This more fine-grained analysis would also potentially inform the section describing the evolution/conservation of sex-biased expression: I expect there must be genes with conserved expression specifically in ovaries or testes (these are ancient animal structures!) but these may have been excluded by the requirement that genes be sex-biased and expressed in at least two organs.

There are at least three examples of statements in the discussion that at the moment misinterpret the experimental results.

The discussion frames the results in the context of sexual selection and sexually antagonistic selection, but these concepts are not synonymous. Sexual selection can shape phenotypes that are specific to one sex, causing no antagonism; and fitness differences between males and females resulting from sexually antagonistic variation in somatic phenotypes may not be acted on by sexual selection. Furthermore, the conditions promoting and consequence of both kinds of selection can be different, so they should be treated separately for the purposes of this discussion.

The discussion claims that "Our data show that sex-biased gene expression evolves extremely fast" but a comparison or expectation for the rate of evolution is not provided. Many other studies have used comparative transcriptomics to estimate rates of gene expression evolution between species, including mice; are the results here substantially and significantly different from those previous studies? Furthermore, the experimental design does not distinguish between those gene expression phenotypes that are fixed between species as compared to those that are polymorphic within one or more species which prevents straightforward interpretation of differences in gene expression as interspecific differences.

The conclusion that "Our results show that most of the genetic underpinnings of sex differences show no long-term evolutionary stability, which is in strong contrast to the perceived evolutionary stability of two sexes" - seems beyond the scope of this study. This manuscript does not address the genetic underpinnings of sex differences (this would involve eQTL or the like), rather it looks at sex differences in gene expression phenotypes. Simply addressing the question of phenotypic evolutionary stability would be more informative if genes expressed specifically in reproductive tissues were separated from somatic sex-biased genes to determine if they show similar patterns of expression evolution.

Reviewer #3 (Public Review):

This manuscript reports some interesting and important patterns. The results on sex-bias in different tissues and across four taxa would benefit from alternative (or additional) presentation styles. In my view, the most important results are with respect to alpha (fraction of beneficial amino acid changes) in relation to sex-bias (though the authors have made this as a somewhat minor point in this version).

The part that the authors emphasize I don't find very interesting (i.e., the sexes have overlapping expression profiles in many nongonadal tissues), nor do I believe they have the appropriate data necessary to convincingly demonstrate this (which would require multiple measures from the same individual).

This study reports several interesting patterns with respect to sex differences in gene expression across organs of four mice taxa. An alternative presentation of the data would yield a clearer and more convincing case that the patterns the authors claim are legitimate.

I recommend that the authors clarify what qualifies as "sex-bias".

Author response:

We appreciate the time of the reviewers and their detailed comments, which will help to improve the manuscript.

We are sorry that at least one reviewer seems to have had the impression that we have conflated issues about gonadal and non-gonadal sex phenotypes. This referee suggests that we should use Sharpe et al. (2023) to develop our concepts. However, what is discussed in Sharpe et al. was already the guiding principle for our study (without knowing this paper before). In our paper, we introduce the gonadal binary sex (which is self-evidently also the basis for creating the dataset in the first place, because we needed to separate males from females) and go then on to the question of (adult) sex phenotypes for the rest of the paper. The gonadal data are included only as comparison for contrasting the patterns in the non-gonadal tissues.

Our study presents the largest systematic dataset so far on the evolution of sex-biased gene expression. It is also the first that explores the patterns of individual variation in sex-biased gene expression and the SBI is an entirely new procedure to directly visualize these variance patterns in an intuitive way (note that the relative position of the distributions along the X-axis is indeed not relevant). The results are actually quite nuanced (e.g. the rather dynamv changes seen in mouse kidney and liver comparisons) and go certainly beyond what would have been predictable based on the current literature.

Also, we should like to point out that our study contradicts recent conclusions that were published in high profile journals, that had suggested that a substantial set of sex-biased genes has conserved functions between humans and mice and that mice can therefore be informative for gender-specific medicine studies. Our data suggest that that only a very small set of genes are conserved in their sex-biased expression. These are epigenetic regulator genes and it will therefore be interesting in the future to focus on their roles in generating the differences between sexual phenotypes in given species.

We will be happy to use the referee comments to clarify all of these points in a revised version. But we do not think that our "evidence is incomplete" and that there are several "overstated key conclusions". We have used all canonical statistical analyses that are typically used in papers of sex-biased gene expression, as acknowledged by reviewers 1 and 2. The additional statistical analyses that are requested are not within the scope of such papers, but could be subject to separate general studies, independent of the sex-bias analysis (e.g. the role of highly expressed genes versus low expressed genes, or the analysis of the fraction of neutrally evolving loci).

Finally, it is unclear why the overall rating of the paper is at the lowest possible category ("useful study"), given that it adds a substantial amount of data and new insights into the exploration of the non-binary nature of sexual phenotypes.

eLife assessment

This paper provides valuable findings related to the impact and timing of exogenous interleukin 2 on the balance of exhausted (Tex) versus effector (Teff) that differentiate from precursors T cells (Tpex) during chronic viral infection. While the data appear solid, the overall claims that IL-2 suppresses Tpex are only partially supported, with the rationale for the timing of IL-2 treatment and its underlying mechanisms remaining unclear.

Reviewer #1 (Public Review):

Summary:

The title states "IL-2 enhances effector function but suppresses follicular localization of CD8+ T cells in chronic infection" which data from the paper show but does not seem to be the major goal of the authors. As stated in the short assessment above, the goal of this work seems to connect IL-2 signals, mostly given exogenously, to the differentiation of progenitor T cells (TPEX) that will help sustain effector T cell responses against chronic viral infection (TEX/TEFF). The authors mostly use chronic LCMV infection in mice as their model of choice, Flow cytometry, fluorescent microscopy, and some in vitro assays to explore how IL2 regulates TPEX and TEX/TEFF differentiation. Gain and loss of functions experiments are also conducted to explore the roles of L2 signaling and BLIMP-1 in regulating these processes. Lastly, a loose connection of their mouse findings on TPEX/TEX cells to a clinical study using low-dose IL-2 treatment in SLE patients is attempted.

Strengths:

(1) The impact of IL-2 treatment of TPEX/TEX differentiation is very clear.

(2) The flow cytometry data are convincing and state-of-the-art.

Weaknesses:

(1) The title appears disconnected from the major focus of the work.

(2) The number of TPEX cells is not changed. IL2 treatment increases the number of TEFF and the proportion of TPEX is lower suggesting it does not target TPEX formation. The conclusion about an inhibitory role of IL2 treatment on TPEX formation seems therefore largely overstated.

(3) Are the expanded TEX/TEFF cells really effectors? Only GrB and some cell surface markers are monitored (44, 62L). Other functions should be included, e.g., CD107a, IFNg, TNF, chemokines - Tbet?

(4) The rationale for IL2 treatment timing is unclear. Seems that this is given at the T cell contraction time and this is interesting compared to the early treatment that ablate TPEX generation. Maybe this should really be explored further?

(5) The TGFb/IL6/IL2 in vitro experiment does not bring much to the paper.

(6) The Figure 2 data try to provide an explanation for a prior lack of difference in viral titers after IL2 treatment. It is hard to be convinced by these tissue section data as presented. It also begs the question of how the host would benefit from the low dose IL-2 treatment if IL-2 TEFF are not contributing to viral control as a result of their inappropriate localization to viral reservoirs.

(7) It is unclear what the STA5CA and BLIMP-1 KO experiments in Figure 3 add to the story that is not already expected/known.

(8) The connection to the low-dose IL2 treatment in SLE patients is very loose and weak. This version is likely not the ligand that preferentially signals to CD122 either. SLE is different from a chronic viral infection and the question of timing seems critical from all the data shown in this manuscript. So it is very difficult to make any robust link to the mechanistic data.

(9) It is really unclear what the take-home message is. IL-2 is signaling via STAT5 and BLIMP1 is also a known target as published by many groups including this one, and these results are more than expected. The observation that TEFF may be differentially localized in the WP area is interesting but no mechanisms are really provided (guessing CXCR5 but again expected). Also, all these observations are highly dependent on the timing of IL2 administration which is fascinating but not explored at all. It also limits significance since underlying mechanisms are unknown and we do not know when such treatment would have to be given.

Reviewer #2 (Public Review):

This study utilized the LCMV Docile infection model, which induces chronic and persistent infection in mice, leading to T cell exhaustion and dysfunction. Through exogenous IL-2 fusion protein treatment during the late stage of infection, the researchers found that IL-2 treatment significantly enlarges the antigen-specific effector CD8 T cells, expanding the CXCR5-TCF1- exhausted population (Tex) while maintaining the size of the CXCR5+TCF1+ precursors of exhausted T cell population (Tpex). This preservation of the Tpex population's self-renewing capacity allows for sustained T cell proliferation and antiviral responses.

The authors discovered a dual effect of IL-2 treatment: it decreases CXCR5 expression on Tpex cells, restricting their entry into the B cell follicle. This may explain why IL-2 treatment has little impact on overall viral control. However, this finding also suggests a potential application of IL-2 treatment for autoimmune diseases, as it can suppress specific immune responses within the B cell follicle. Using imaging-based approaches, the team provided direct evidence that IL-2 treatment shifts the viral load to concentrate within the B cell follicle, correlating with the observed decrease in CXCR5 expression.

Further, the researchers showed that ectopic expression of constitutively active STAT5, downstream of IL-2 induced cytokine signaling, in P14 TCR transgenic T cells (specific for an LCMV epitope), drove the T cell population toward the CXCR5- Tex phenotype over the CXCR5+ Tpex cells in vivo. Additionally, abrogating Blimp1, upregulated by active IL-2-phosphorylated STAT5 signaling, restored the CXCR5+ Tpex population.

Building on these results, the researchers used an engineered IL-2 fusion protein, ANV410, targeting the beta-chain of the IL-2 receptor CD122, which successfully replicated their earlier findings. Importantly, the Tpex-sustaining effect of IL-2 was only observed when treatment was administered during the late stage of infection, as early treatment suppressed Tpex cell generation. Immune profiling of SLE patients undergoing low-dose IL-2 treatment showed a similar reduction in the CXCR5+ Tpex cell population.

This study provides compelling data on the physiological consequences of IL-2 treatment during chronic viral infection. By leveraging the chronic and persistent LCMV Docile infection model, the researchers identified the temporal effects of IL-2 fusion protein treatment, offering strategic insights for therapies targeting cancer and autoimmune diseases.

eLife assessment

This is a mechanistic study showing the effect of combining inhibition of autophagy (through ULK1/2) and KRAS (using sotorasib) on KRAS mutant NSCLC making the study valuable to cancer biologists and more broadly in a clinical setting. The evidence generated by GEM mouse models and cell lines is solid but could be further strengthened by increasing the mouse cohort size. This study holds translational relevance beyond NSCLC to other indications that carry KRAS mutations.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Ghazi et reported that inhibition of KRASG12C signaling increases autophagy in KRASG12C expressing lung cancer cells. Moreover, the combination of DCC 3116, a selective ULK1/2 inhibitor, plus sotorasib displays cooperative/synergistic suppression of human KRASG12C driven lung cancer cell proliferation in vitro and tumor growth in vivo. Additionally, in genetically engineered mouse models of KRASG12C driven NSCLC, inhibition of either KRASG12C or ULK1/2 decreases tumor burden and increases mouse survival. Additionally, this study found that LKB1 deficiency diminishes the sensitivity of KRASG12C/LKB1Null-driven lung cancer to the combination treatment, perhaps through the emergence of mixed adeno/squamous cell carcinomas and mucinous adenocarcinomas.

Strengths:

Both human cancer cells and mouse models were employed in this study to illustrate that inhibiting ULK1/2 could enhance the responsiveness of KRASG12C lung cancer to sotorasib. This research holds translational importance.

Weaknesses:

The revised manuscript has addressed most of my previous concerns. However, I still have one issue: the sample size (n) for the GEMM study in Figures 4E and 4F is too small, despite the authors' explanation. The data do not support the conclusion due to the lack of significant difference in tumor burden. Additionally, the significance labels in Figure 4E are not clearly explained.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Given that KRAS inhibition approaches are a relatively new innovation and that resistance is now being observed to such therapies in patients with NSCLC, investigation of combination therapies is valuable. The manuscript furthers our understanding of combination therapy for KRAS mutant non-small cell lung cancer by providing evidence that combined inhibition of ULK1/2 (and therefore autophagy) and KRAS can inhibit KRAS-mutant lung cancer growth. The manuscript will be of interest to the lung cancer community but also to researchers in other cancer types where KRAS inhibition is relevant.

Strengths:

The manuscript combines cell line, cell line-derived xenograft, and genetically-engineered mouse model data to provide solid evidence for the proposed combination therapy.  The manuscript is well written, and experiments are broadly well performed and presented.

We thank Reviewer #1 (R1) for the generally favorable review of our manuscript, and also for the more detailed critique that identifies potential weaknesses in the research, which we address on a point-by-point basis below. 

Weaknesses:

With 3-4 mice per group in many experiments, experimental power is a concern and some comparisons (e.g. mono vs combination therapy) seem to be underpowered to detect a difference. Both male and female mice are used in experiments which may increase variability.

We thank R1 for pointing out concerns regarding statistical power in our various mouse models of NSCLC experiments, and agree that more mice per group would certainly increase statistical power.  However, there are certain logistical considerations that impact the generation of cohorts of experimental KrasLSL-G12C mice.  Because mice homozygous for the KrasLSL-G12C allele display embryonic lethality, we are required to generate experimental mice by crossing heterozygous male and female KrasLSL-G12C mice.  Although 66% of the progeny of such crosses are predicted to be KrasLSL-G12C/+, experience tells us that we only obtain ~40-50% heterozygous KrasLSL-G12C/+ mice with litter sizes around 6-8 mice from such crosses.  Therefore, there are usually only about 4 heterozygous KrasLSL-G12C mice per litter, which presents a substantial challenge in generating larger cohorts of age-matched mice suitable for experiments, especially under conditions where we wish to euthanize mice at multiple time points for analysis.  For the GEM model experiments, Figure 3B is the only experiment that has n=3.  All other experiments contain 4-6 mice per experimental condition.  We rationalized using both male and female mice because both human males and females have high lung cancer rates.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Ghazi et reported that inhibition of KRASG12C signaling increases autophagy in KRASG12C-expressing lung cancer cells. Moreover, the combination of DCC 3116, a selective ULK1/2 inhibitor, plus sotorasib displays cooperative/synergistic suppression of human KRASG12C-driven lung cancer cell proliferation in vitro and tumor growth in vivo. Additionally, in genetically engineered mouse models of KRASG12C-driven NSCLC, inhibition of either KRASG12C or ULK1/2 decreases tumor burden and increases mouse survival. Additionally, this study found that LKB1 deficiency diminishes the sensitivity of KRASG12C/LKB1Null-driven lung cancer to the combination treatment, perhaps through the emergence of mixed adeno/squamous cell carcinomas and mucinous adenocarcinomas.

Strengths:

Both human cancer cells and mouse models were employed in this study to illustrate that inhibiting ULK1/2 could enhance the responsiveness of KRASG12C lung cancer to sotorasib. This research holds translational importance.

We thank Reviewer #2 (R2) for the generally favorable review of our manuscript, and also for the more detailed critique that identifies potential weaknesses in the research, which we address on a point-by-point basis below. 

Weaknesses:

Additional validation of certain data is necessary.

(1) mCherry-EGFP-LC3 reporter was used to assess autophagy flux in Figure 1A. Please explain how autophagy status (high, medium, and low) was defined. It's also suggested to show WB of LC3 processing in different treatments as in Figure 1A at 48 hours.

We thank the reviewer for this comment and agree that a more thorough description of how autophagy status is assessed using the Fluorescent Autophagy Reporter (FAR) would benefit the readers of our manuscript.  Cells engineered to express the FAR are analyzed by flow cytometry in which we defined autophagy status by gating viable (based Sytox Blue staining), DMSO-treated control cells into three bins based on the ratio of EGFP:mCherry fluorescence.  We gate all live cells into the 33% highest EGFP-positive cells (autophagy low) and the 33% highest mCherry-positive cells (autophagy high), and therefore, the proportion in the middle is also approximately 33% and considered the medium autophagy status.  Again, these gates are based entirely on the DMSO-treated control cells, and all other treatments within the experiment are compared to settings on these gates.  In response to a specific manipulation (sotorasib, trametinib, DCC-3116 etc) we assess how the specific treatment changes the percentages of cells in each of the pre-specified gates to assess increased autophagy (decreased EGFP:mCherry ratio) or decreased autophagy (increased increased EGFP:mCherry ratio). 

Although LC3 processing and/or the expression of p62SQSTM1 are used by others as markers of autophagy, there is much debate in the literature as to how reliable immunoblotting analysis of LC3 processing or p62SQSTM1 expression are as measures of autophagy.  Certainly, in our hands, we find that the Fluorescent Autophagy Reporter is a much more sensitive measure of changes in autophagy in various different cancer cell lines as we have described in previous papers (Kinsey et al., PMID: 30833748, Truong et al., PMID: 32933997 and Silvis & Silva et al., PMID: 36719686).  Furthermore, in the omnibus publication that describes techniques for measuring autophagy (Klionsky et al., PMID: 33634751) the use of the FAR (or similarly configured reporters) is regarded as the gold standard for measuring autophagy status in cells.  We have amended the Materials & Methods section of our manuscript to better describe the use of the FAR in measuring autophagy. 

(2) For Figures 1J, K, and L, please provide immunohistochemistry (IHC) images demonstrating RAS downstream signaling blockade by sotorasib and autophagy blockade by DCC 3116 in tumors.

We thank the reviewer for the comment and have probed the tumors from the xenograft experiments in Figures 1J, K, and L for pERK1/2 and p62SQSTM1 to determine the biochemical activity of sotorasib or DCC-3116, respectively and have provided representative images below. We observed the expected decrease in pERK and p62 signal after sotorasib treatment in all three xenografted cell lines. We did observe the expected accumulation of p62 in the DCC-3116 treated tumors from the NCI-H2122 and NCI-H358 cell lines. There appears to be no difference between the vehicle and DCC-3116 treated tumors in the NCI-H358 cell line-derived tumors as detected by IHC.

Author response image 1.

(3) Given that both DCC 3116 and ULK1K46N exhibit the ability to inhibit autophagy and synergize with sotorasib in inhibiting cell proliferation, in addition to demonstrating decreased levels of pATG13 via ELISA assay, please include Western blot analyses of LC3 or p62 to confirm the blockade of autophagy by DCC 3116 and ULK1K46N in Figure 1 & Figure 2.

We appreciate the reviewer's comment and have performed an immunoblot analysis of cells treated with DCC-3116 or expressing ULK1K46N and probed for p62SQSTM1 and LC3 expression.  We did observe the expected accumulation of p62 SQSTM1 in NCI-H2122 (ULK1K46N) cells treated with 1ug/ml doxycycline to induce expression of ULK1K46N compared to DMSO treatment.  Additionally, we treated the human cell lines from Figure 1 with sotorasib and/or DCC-3116 and tested for p62SQSTM1 expression after 48 hours of treatment. In the human cell lines NCI-H2122 and NCI-H358, there was a decrease in the p62 signal with increasing doses of sotorasib, as expected. There was no detectable change in p62 levels in the Calu-1 cells by immunoblot. For LC3-I/LC3-II, there was only one detectable band in the NCI-H2122 cells, which makes it difficult to interpret the results and further emphasizes why we use the fluorescent autophagy reporter which is more sensitive than immunoblotting. There is no detectable change in LC3-I/LC3-II in the Calu-1 cells treated with increasing doses of sotorasib, but the expected decrease in LC3-I is observed with sotorasib treatment in the NCI-H358 cells.

Author response image 2.

(4) Since adenocarcinomas, adenosquamous carcinomas (ASC), and mucinous adenocarcinomas were detected in KL lung tumors, please conduct immunohistochemistry (IHC) to detect these tumors, including markers such as p63, SOX2, Katrine 5.

We have included IHC analysis of the adenosquamous carcinomas for the markers p63, SOX2, and Keratin 5 from the KL mouse in Figure 3 and the ASC tumors in Supplemental Figure 4, and thank the reviewer for this excellent suggestion. The straining for these markers is below. Of note, we tried two different SOX2 antibodies (cell signaling technologies #14962 and cell signaling technologies # 3728) and could not detect any staining in any section.

Author response image 3.

(5) Please provide the sample size (n) for each treatment group in the survival study (Figure 4E). It appears that all mice were sacrificed for tumor burden analysis in Figure 4F. However, there doesn't seem to be a significant difference among the treatment groups in Figure 4F, which contrasts with the survival analysis in Figure 4E. It is suggested to increase the sample size in each treatment group to reduce variation.

We have updated Figure 4E to indicate sample size for each treatment group and thank the reviewer for this suggestion.  Any mice that remained on study through the entire 8-week treatment regimen were sacrificed after the last day of treatment (Day 56).  Figure 4F indicates analysis of total tumor burden in all mice that remained on treatment for the full 8 weeks and mice that reached euthanasia criteria before the end of the 8-week treatment.  Therefore, it is important to note that the mice in Figure 4F were not all euthanized on the same day.  There is no statistically significant difference between the 3 treatment groups (sotorasib, DCC-3116, combination).  This may be due to a lower sample size as well as ending the treatment at 8 weeks as opposed to continuing the treatment for a longer period of time.  Although we agree that increasing the sample size would benefit the study, due to how long the GEMM model experiments take (12-16 weeks of breeding, 6 weeks for the mice to reach adulthood, 10 weeks of tumor formation post-initiation, 8 weeks of treatment= ~40 weeks) we would respectfully submit that the analysis of additional mice is outside the scope of the current revised manuscript.

(6) In KP mice (Figure 5), it seems that a single treatment alone is sufficient to inhibit established KP lung tumor growth. Combination treatment does not further enhance anti-tumor efficacy. Therefore, this result doesn't support the conclusion generated from human cancer cell lines. Please discuss.

We thank the reviewer for this observation.  Indeed, KP lung tumors were sensitive to single agent DCC-3116 treatment, which is reflected in the tumor burden analysis.  This was somewhat surprising to us as we have not previously detected much anti-tumor activity using 4-amino-quinoloines (chloroquine or hydroxychloroquine) or other autophagy inhibitors.  It should be noted however that the KRASG12C/TP53R175H NSCLC model has a very low tumor burden overall (~4% in vehicle-treated mice).  Additionally, our microCT imager cannot detect AAH and small tumors at the settings/resolution used.  Therefore, we were limited in our ability to detect small tumors or hyperplasia by microCT imaging.  Although there was a decrease in overall tumor burden with single agent DCC-3116 treatment, we could not demonstrate using microCT imaging that KRASG12C/TP53R175H lung tumors were actually regressing with single agent DCC-3116 treatment.  The larger tumors that were detected appeared to show a cytostatic effect (i.e. no or slow growth) with DCC-3116 monotherapy.  This may reflect our inability to detect regression of AAH or small tumors with the microCT.  In all human cell lines tested, the only cell line that responded to single agent DCC-3116 treatment was NCI-H358 cells, which do have a complete heterozygous loss of the TRP53 gene and lack TP53 protein.  However, other cells that also have a loss of expression of TP53 expression (Calu-1) are insensitive to single-agent DCC-3116 treatment. Due to the low mutational burden of the KP mouse model compared to human NSCLC cell lines driven by mutationally-activated KRASG12C and the loss of TP53 function, it is difficult to directly compare GEM models to the human cell line models.  Most of the human cell lines have alterations in other genes that are not altered in the KP mouse model which could affect the sensitivity of treatment.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor comments:

(1) Figure legends are currently not adequate - information about the number and nature of replicates, stats, and definitions of the labelling used for stats should be added throughout. In Figure 5B, only two lines of four are labelled with * or ns.

We thank the reviewer for this comment and have included more details in the figure legends that describe replicates, statistical analysis and definitions of labeling.  We also note that the methods section has a detailed description of the statistical analysis used.

(2) What statistical test is performed on Figure 5E to get a p < 0.05 between the vehicle and DCC group?

We performed a one-way ANOVA for all statistical analyses with more than 2 experiential groups. We thank the reviewer for pointing out this typo. These data points (vehicle vs. DCC-3116) are not statistically significant, which has been revised in the figure.

(3) The manuscript figures would be improved by the use of a colourblind-friendly palette.

We have previously published multiple manuscripts using this color scheme for the fluorescent autophagy reporter experiments and chose to use red and green as the reporter uses EGFP and mCherry.  We wanted to keep this color scheme consistent across our publications and would prefer not to change the colors.  However, we agree with the reviewer that the data should be accessible to all people and, therefore, have updated these graphs to include slashes over the red color to ease in telling the differences between the red and green colors.  Thank you to the reviewer for this excellent suggestion.

(4) The manuscript should be fully checked for mouse (sentence case) and human (caps) gene (italics) and protein (non-italics).

In this manuscript we are using the nomenclatures approved by the HUGO Gene Nomenclature Committee (https://en.wikipedia.org/wiki/HUGO_Gene_Nomenclature_Committee) in which:

Human genes are written as KRAS, TP53 etc i.e. ITALICIZED CAPS

Mouse genes are written as Kras, Trp53 etc:  i.e. Italicized and sentence case

Human and mouse proteins are written as KRAS, TP53 etc:  i.e. NON-ITALICIZED CAPS

In response to the reviewer’s suggestion, we have gone through the manuscript to check for this and make any appropriate changes.  Of note, we intentionally refer to the mouse protein changes as KRASG12C/LKB1null or KRASG12C/TP53R172H (capitalized), as this references the protein change and not the nucleotide change that occurs in the gene.

(5) Adenosquamous is the correct term for the disease.  In parts, it's referred to as adeno/squamous or adeno-squamous.  The abbreviation ADC is also defined many times.

Thank you to the reviewer for this comment.  We have corrected the manuscript text to only use adenosquamous and only define ADC in the first instance.

(6) Line 434 - "as previously described" but no reference.

Typos:

(1) Line 117 – either

(2) Line 314 – synergistic

(3) Line 317 – therefore

(4) Line 502 – medium

We thank the reviewer for pointing out these typos and have modified the text appropriately.

Reviewer #2 (Recommendations For The Authors):

(1) The statement on Page 4, Lines 119-120, lacks clarity: 'Furthermore, LKB1 silencing diminishes the sensitivity of KRASG12C/LKB1Null-driven lung cancer perhaps through the emergence of mixed adeno/squamous cell carcinomas and mucinous adenocarcinomas.  It is unclear whether this refers to the sensitivity to the combination treatment or to the KRASc inhibitor alone.

We thank the reviewer for this comment and agree that the statement lacks clarity.  The intent of this statement was to refer to both single agent sotorasib treatment as well as the combination with DCC-3116.  

(2) Page 5 Line 147 "KRASG12X ". Please correct this typo.

We thank the reviewer for this comment, but this is not a typo. We intended for this line to state KRASG12X to refer to cell lines with any KRASG12 alteration, e.g KRASG12D, KRASG12C, KRASG12S, KRASG12R etc.  

(3) The color of the dots in Figure 5B labeling does not match the dots in the graph.

For all bar graphs in the manuscript, the dots representing individual mice are black, and the bar itself is color-coded based on treatment type. The dots in Figure 5B follow this pattern and are intended to be this way.

(4) Figure 5C depicts lung weight rather than tumor growth, contrary to the text description "regression of pre-existing lung tumors was detected by microCT scanning (Figure 5C, Figure S5)".

Figure 5C does not depict lung weight but the percent body weight change in treated mice, described in the figure legend.  We thank the reviewer for pointing this out because we referenced the wrong panel in the text.  The figures referenced should be Figure 5B, Figure S5.  We have corrected this in the text.

Reviewer #1 (Public Review):

Summary:

The authors profile gene expression, chromatin accessibility and chromosomal architecture (by Hi-C) in activated CD4 T cells and use this information to link non-coding variants associated with autoimmune diseases with putative target genes. They find over a 1000 genes physically linked with autoimmune disease loci in these cells, many of which are upregulated upon T cell activation. Focusing on IL2, they dissect the regulatory architecture of this locus, including the allelic effects of GWAS variants. They also intersect their variant-to-gene lists with data from CRISPR screens for genes involved in CD4 T cell activation and expression of inflammatory genes, finding enrichments for regulators. Finally, they showed that pharmacological inhibition of some of these genes impacts T cell activation.

This is a solid study that follows a well-established canvas for variant-to-gene prioritisation using 3D genomics, applying it to activated T cells. The authors go some way in validating the lists of candidate genes, as well as explore the regulatory architecture of a candidate GWAS locus. Jointly with data from previous studies performing variant-to-gene assignment in activated CD4 T cells (and other immune cells), this work provides a useful additional resource for interpreting autoimmune disease-associated genetic variation.

Autoimmune disease variants were already linked with genes in CD28-stimulated CD4 T cells using chromosome conformation capture, specifically Promoter CHi-C and the COGS pipeline (Javierre et al., Cell 2016; Burren et al., Genome Biol 2017; Yang et al., Nat Comms 2020). The authors cite these papers and present a comparative analysis of their variant-to-gene assignments (in addition to scRNA-seq eQTL-based assignments). Furthermore, they find that the Burren analysis yields a higher enrichment for gold standard genes.

I thank the authors for their revisions in response to my initial review. The revised version now includes a more comprehensive comparative analysis of different datasets and V2G approaches and discusses the potential sources of differences in the results. Most significantly, the authors have now included an interesting comparison of their methodology with the popular ABC technique and outlined the key limitations of ABC relative to their method and other (Capture) Hi-C-based V2G approaches.

eLife assessment

This is a solid study that follows a well-established canvas for variant-to-gene prioritisation using 3D genomics, applying it to activated T cells. The authors go some way in validating the lists of candidate genes, as well as exploring the regulatory architecture of a candidate GWAS locus. Jointly with data from previous studies performing variant-to-gene assignment in activated CD4 T cells (and other immune cells), this work provides a useful additional resource for interpreting autoimmune disease-associated genetic variation.

Reviewer #2 (Public Review):

Summary:

There is significant interest in characterizing the mechanisms by which genetic mutations linked to autoimmunity perturb immune processes. Pahl et al. collect information of dynamic accessible regions, genes, and 3D contacts in primary CD4+ T cell samples that have been stimulated ex vivo. The study includes a variety of analyses characterizing these dynamic changes. With TF footprinting they propose factors linked to active regulatory elements. They compare the performance of their variant mapping pipeline that uses their data versus existing datasets. Most compelling there was a deep dive into additional study of regulatory elements nearby the IL2 gene. Finally, they perform a pharmacological screen targeting several genes they suggest are involved in T cell proliferation.

Strengths:

- The work done characterizing elements at the IL2 locus is impressive.

Weaknesses:

- There are extensive studies performed on resting and activated immune cell states (CD4+ T cells and other cell types) and some at multiple time points or concentrations of stimuli that collect ATAC-seq and/or RNA-seq. Several analyses performed in published studies were similarly performed in this study. I expected the authors to at least briefly mention published studies and whether their conclusions generally agree or disagree. Are the same dynamic regulatory regions or genes identified upon T cell activation? Are the same TF footprints enriched in these dynamic regulatory elements? In the revision, I appreciate that the authors now include additional data from several studies that I had initially suggested for the purposes of nominating disease genes in their precision-recall analysis.

Reviewer #3 (Public Review):

Summary:

This paper used RNAseq, ATACseq, and Hi-C to assess gene expression, chromatin accessibility, and chromatin physical associations for native CD4+ T cells as they respond to stimulation through TCR and CD28. With these data in hand, the author identified 423 GWAS signals to their respective target genes, where most of these were not in the proximal promoter, but rather distal enhancers. The IL-2 gene was used as an example to identify new distal cis regulatory regions required for optimal IL-2 gene transcription. These distal elements interact with the proximal IL2 promoter region. When the distal enhancer contained an autoimmune SNP, it affected IL-2 gene transcription. The authors also identified genetic risk variants that were associated to genes upon activation. Some of these regulate proliferation and cytokine production, but others were novel.

Strengths:

This paper provides a wealth of data related to gene expression after CD4 T cells are activated through the TCR and CD28. An important strength of this paper is that these data were intensively analyzed to uncover autoimmune disease SNPs in cis acting regions. Many of these could be assigned to likely target genes even though they often are in distal enhancers. These findings help to provide a better understanding concerning the mechanism by which GWAS risk elements impact gene expression.

Another strength to this study was the proof-of-principle studies examining the IL-2 gene. Not only were new cis acting enhancers discovered, but they were functionally shown to be important in regulating IL-2 expression, including susceptibility to colitis. Their importance was also established with respect to such distal enhancers harboring disease relevant SNPs, which were shown to affect IL-2 transcription.

The data from this study were also mined against past Crispr screens that identified genes that control aspects of CD4 T cell activation. From these comparisons, novel genes were identified that function during T cell activation.

Weaknesses:

A weakness from this study is that few individuals were analyzed, i.e., RNAseq and ATACseq (n=3) and HiC (n=2). Thus, the authors may have underestimated potentially relevant risk associations by their chromatin capture-based methodology. This might account for low overlap of their data with the eQTL-based approach or the HIEI truth set.

The authors explain that the low overlap is not due to few GWAS associations by HiC. The expanded discussion in the revised manuscript provides a framework to help explain inherent differences between these methods that may contribute to the low overlap.

Impact:

This study indicates that defining distal chromatin interacting regions help to identify distal genetic elements, including relevant variants, that contribute to gene activation.

Author response:

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

Reviewer #1 (Public Review): 

Summary:

The authors profile gene expression, chromatin accessibility, and chromosomal architecture (by Hi-C) in activated CD4 T cells and use this information to link non-coding variants associated with autoimmune diseases with putative target genes. They find over 1000 genes physically linked with autoimmune disease loci in these cells, many of which are upregulated upon T cell activation. Focusing on IL2, they dissect the regulatory architecture of this locus, including the allelic effects of GWAS variants. They also intersect their variant-to-gene lists with data from CRISPR screens for genes involved in CD4 T cell activation and expression of inflammatory genes, finding enrichments for regulators. Finally, they showed that pharmacological inhibition of some of these genes impacts T-cell activation. 

This is a solid study that follows a well-established canvas for variant-to-gene prioritisation using 3D genomics, applying it to activated T cells. The authors go some way in validating the lists of candidate genes, as well as exploring the regulatory architecture of a candidate GWAS locus. Jointly with data from previous studies performing variant-to-gene assignment in activated CD4 T cells (and other immune cells), this work provides a useful additional resource for interpreting autoimmune disease-associated genetic variation. 

Suggestions for improvement:

Autoimmune disease variants were already linked with genes in CD28-stimulated CD4 T cells using chromosome conformation capture, specifically Promoter CHi-C and the COGS pipeline (Javierre et al., Cell 2016; Burren et al., Genome Biol 2017; Yang et al., Nat Comms 2020). The authors cite these papers and present a comparative analysis of their variant-to-gene assignments (in addition to scRNA-seq eQTL-based assignments). Furthermore, they find that the Burren analysis yields a higher enrichment for gold standard genes. 

The obvious question that the authors don't venture into is why the results are quite different. In principle, this could be due to the differences between: 

(a) the cell stimulation procedure 

(b) the GWAS datasets used 

(c)  the types of assay (Hi-C vs Capture Hi-C) 

(d) approaches for defining gene-linked regions (loops vs neighbourhoods) 

(e) how the GWAS signals at gene-linked regions are aggregated (e.g., the flavours of COGS in Javierre and Burren vs the authors' approach)

Re (a), I'm not sure the authors make it explicitly clear in the main text that the Capture Hi-Cbased studies also use *stimulated* CD4 T cells, particularly in the section "Comparative predictive power...". So the cells used are pretty much the same, and the differences likely arise from points (b) to (e).

It would be useful for the community to understand more clearly what is driving these differences, ideally with some added data. Could the authors, for example, take the PCHi-C data from Javierre/Burren and use their GWAS data and variant-to-gene assignment algorithms? 

We greatly appreciate the referee’s expert assessment of our work and its value to the field, and we are glad that the referee was enthused by our comparison of the predictive power of the various V2G approaches. A point not emphasized enough in the original version of the manuscript is that we actually did harmonize the various datasets in the way the referee suggests for the precision/recall analysis. We took the contact maps presented from each paper, mapped genes using the same set of GWAS SNPs, and defined all gene-linked regions using our loop calling approach. This has been clarified in the revised version of the manuscript. We have now included a more thoughtful discussion of the possible sources of discrepancy between the different studies included in the comparison, and our thoughts on the potential sources raised by the referee are outlined below:

(a) The modes of stimulation used are similar between studies, but timepoints and donors did vary, and ours was the only study that sorted naïve CD4+ T cells before stimulation. These aspects could represent a source of variability. 

(b) The GWAS is not a source of variability because we re-ran the raw data from all the orthogonal studies through our V2G pipeline using the same GWAS as in the current manuscript. 

(c) The use of HiC vs. Capture HiC is a likely source of variability. The Capture-HiC datasets included in our comparison are lower resolution (i.e. HindIII) but focus higher sequencing depth at promoters compared to our HiC datasets – i.e., Capture-HiC may mis-call loops to the wrong promoters due to lower resolution as we have shown in our previous study [Su, Human Genetics, 2021], and will miss distal SNP interactions at promoters not included in the capture set. While HiC is unbiased in this regard, HiC will fail to call some SNP-promoter loops called by CaptureHiC because the sequencing power is not specifically focused at promoters. 

(d) For studies using neighborhood approaches, we re-ran the raw data through our loop calling algorithm to connect distal SNP to gene promoters, and regarding (e) above, we ran the raw data through our V2G pipeline to allow a better comparison.

In addition, given that the authors use Hi-C, a popular method for V2G prioritisation for this type of data is currently ABC (Nasser et al, Nature 2021). Could the authors provide a comparative analysis with respect to the V2G assignments in the paper and, if they see it appropriate, also run ABC-based GWAS integration on their own Hi-C data?

This is an excellent suggestion, which we have followed in the revised version of our manuscript. It should be noted (and we do so in the text of the revision) that there is an important caveat to bringing in the ABC model. Chromosome conformation-based approaches are biologically constrained (i.e., informed) by the natural structure of chromatin in the nucleus that controls how gene transcription is regulated in cis, and it does so in a way that brings value to GWAS data. However, the ABC model further constrains the input data by imposing non-biological filters that allow the algorithm to be applied, but impose artifactual limitations that may negatively impact interpretation and discovery. In addition to filtering out pseudogenes, bidirectional RNA, antisense RNAs, and small RNAs, the ABC model gene set eliminates genes ubiquitously expressed across tissues (based on the assumption that these genes are driven primarily by elements adjacent to their promoters) and only allows annotation of one promoter per gene, even though the median number of promoters per gene in the human genome is three. In contrast, our chromatin-based V2G removes pseudogenes, but includes lincRNA and small RNAs, and includes all alternative transcription start sites annotated by gencode. 

To apply the ABC GWAS gene nomination model to our CD4+ T cell chromatin-based V2G data, we used our ATAC-seq data and publicly available CD4+ T cell H3K27ac ChIP-seq data as input, and integrated this with GWAS and the average ENCODE-derived HiC dataset from the original ABC paper. The activity-by-contact model nominated 650 genes, compared to 1836 genes when using our cell type-matched HiC data and analysis pipeline. Only 357 of these genes were nominated by both approaches; 1479 genes nominated by our approach were not nominated by ABC, while 293 genes not implicated by our approach were newly implicated by ABC. To determine how the ABC-constrained approach performs against the HIEI gold standard set, we subjected all datasets used for the comparison depicted in the new Figure 5D to the same promoter filter used by the ABC model prior as part of the precision-recall re-analysis. Firstly, we found that applying the restricted ABC model promoter annotation to all datasets did not have a large effect on recall, however, the precision of several of the datasets were affected. For example, using the restricted promoter set reduced the precision of our (Pahl) V2G approach and inflated the precision of the nearest gene to SNP metric. Second, the new precision-recall analysis shows that the ABC score-based approach is only half as sensitive at predicting HIEI genes as the chromatin-based V2G approaches. This indicates that constraining GWAS data with cell type- and state-specific 3D chromatin-based data brings more GWAS target gene predictive power than application of the multi-tissue-averaged HiC used by the ABC model. We thank the reviewer for helpful suggestions that have improved the quality of our study.

Reviewer #2 (Public Review): 

Summary:

There is significant interest in characterizing the mechanisms by which genetic mutations linked to autoimmunity perturb immune processes. Pahl et al. collect information on dynamic accessible regions, genes, and 3D contacts in primary CD4+ T cell samples that have been stimulated ex vivo. The study includes a variety of analyses characterizing these dynamic changes. With TF footprinting they propose factors linked to active regulatory elements. They compare the performance of their variant mapping pipeline that uses their data versus existing datasets. Most compelling there was a deep dive into additional study of regulatory elements nearby the IL2 gene. Finally, they perform a pharmacological screen targeting several genes they suggest are involved in T cell proliferation. 

Strengths:

The work done characterizing elements at the IL2 locus is impressive. 

Weaknesses:

Missing critical context to evaluate claims. There are extensive studies performed on resting and activated immune cell states (CD4+ T cells and other cell types) and some at multiple time points or concentrations of stimuli that collect ATAC-seq and/or RNA-seq that have been ignored by this study. How do conclusions from previous studies compare to what the authors conclude here? It is impossible to evaluate the claims without this additional context. These are a few studies I am familiar with (the authors should perform a more comprehensive search to be sure they're not ignoring existing observations) that would be important to compare/contrast conclusions:  o Alasoo, K. et al. Shared genetic effects on chromatin and gene expression indicate a role for enhancer priming in immune response. Nat. Genet. 50, 424-431 (2018). 

- Calderon, D., Nguyen, M.L.T., Mezger, A. et al. Landscape of stimulation-responsive chromatin across diverse human immune cells. Nat Genet 51, 1494-1505 (2019). 

- Gate, R.E., Cheng, C.S., Aiden, A.P. et al. Genetic determinants of co-accessible chromatin regions in activated T cells across humans. Nat Genet 50, 1140-1150 (2018).  o Glinos, D.A., Soskic, B., Williams, C. et al. Genomic profiling of T-cell activation suggests increased sensitivity of memory T cells to CD28 costimulation. Genes Immun 21, 390-408 (2020).  o Gutierrez-Arcelus, M., Baglaenko, Y., Arora, J. et al. Allele-specific expression changes dynamically during T cell activation in HLA and other autoimmune loci. Nat Genet 52, 247-253 (2020). 

- Kim-Hellmuth, S. et al. Genetic regulatory effects modified by immune activation contribute to autoimmune disease associations. Nat. Commun. 8, 266 (2017).  o Ye, C. J. et al. Intersection of population variation and autoimmunity genetics in human T cell activation. Science 345, 1254665 (2014). 

- As a general point, I appreciate it when each claim includes a corresponding effect size and p-value, which helps me evaluate the strength of significance of supporting evidence. 

We greatly appreciate the referee’s expert assessment of our work and emphasis on the value of our functional follow-up studies. Our precision-recall analyses were not meant to represent an exhaustive comparison of all prior GWAS gene nomination studies, although we agree that this could (and should) be done as part of a separate study in a future manuscript. Instead, we focused on gene nomination studies that 1) analyzed resting and activated human CD4+ T cells, 2) whose experimental design was most comparable to our own studies, and 3) had raw data readily available in the appropriate formats to allow re-analysis and harmonization before comparison. This is a point we did not make sufficiently clear in the original version of the manuscript, but have clarified in the revision. 

Based on this rationale, we agree that the studies by Gate et al. and Ye et al. should be included in our comparative precision-recall analysis, and we have done so in the revised manuscript. The Gate study reported ATAC-seq peak co-accessibility, caQTL, eQTL, and HiC data, and we now include the resulting gene nominations from these datasets in the precision-recall analysis. These datasets performed poorly with respect to nomination of HIEI genes, likely due to small sample numbers and low sequencing depth compared to the other eQTL and chromatin capture-based studies. The eQTL reported by Ye et al. nominated 15 genes for autoimmune traits, two of which were in the ‘truth’ HIEI set (IL7R and IL2RB). This resulted low predictive power but a high precision due to the low number of nominated genes compared to the other V2G datasets. As suggested by referee 1, we have also subjected our data to the ‘activity-by-contact’ (ABC) algorithm and have included this dataset in the comparison as well. Please see Figure 5 in the revised manuscript. 

We have elected not to include data from the other studies suggested by the referee for the following reasons: The stimulation paradigm used in the Glinos study is very different from that used in other studies. Also, this study and the study by Calderon did not nominate genes. The studies by Alasoo et al. and Kim-Hellmuth et al. analyzed macrophages, which are not a comparable cell type to CD4+ T cells. The allele-specific eQTL study by Gutierrez-Arcelus et al. included relevant the cell type and activation states, but included a relatively small number of samples (24) and variants (561), and the raw data in dbGAP does not readily allow for re-analysis and harmonization with the other studies. We thank the reviewer for helpful suggestions that have improved the quality of our study.

Reviewer #3 (Public Review): 

Summary:

This paper used RNAseq, ATACseq, and Hi-C to assess gene expression, chromatin accessibility, and chromatin physical associations for native CD4+ T cells as they respond to stimulation through TCR and CD28. With these data in hand, the authors identified 423 GWAS signals to their respective target genes, where most of these were not in the proximal promoter, but rather distal enhancers. The IL-2 gene was used as an example to identify new distal cisregulatory regions required for optimal IL-2 gene transcription. These distal elements interact with the proximal IL2 promoter region. When the distal enhancer contained an autoimmune SNP, it affected IL-2 gene transcription. The authors also identified genetic risk variants that were associated with genes upon activation. Some of these regulate proliferation and cytokine production, but others are novel. 

Strengths:

This paper provides a wealth of data related to gene expression after CD4 T cells are activated through the TCR and CD28. An important strength of this paper is that these data were intensively analyzed to uncover autoimmune disease SNPs in cis-acting regions. Many of these could be assigned to likely target genes even though they often are in distal enhancers. These findings help to provide a better understanding concerning the mechanism by which GWAS risk elements impact gene expression. 

Another strength of this study was the proof-of-principle studies examining the IL-2 gene. Not only were new cis-acting enhancers discovered, but they were functionally shown to be important in regulating IL-2 expression, including susceptibility to colitis. Their importance was also established with respect to such distal enhancers harboring disease-relevant SNPs, which were shown to affect IL-2 transcription. 

The data from this study were also mined against past CRISPR screens that identified genes that control aspects of CD4 T cell activation. From these comparisons, novel genes were identified that function during T cell activation. 

Weaknesses:

A weakness of this study is that few individuals were analyzed, i.e., RNAseq and ATACseq (n=3) and HiC (n=2). Thus, the authors may have underestimated potentially relevant risk associations by their chromatin capture-based methodology. This might account for the low overlap of their data with the eQTL-based approach or the HIEI truth set. 

Impact:

This study indicates that defining distal chromatin interacting regions helps to identify distal genetic elements, including relevant variants, that contribute to gene activation. 

We greatly appreciate the referee’s expert assessment of our work and emphasis on the value of our functional follow-up studies. We have ensured that all sample sizes, effect sizes, p values and FDR statistics are included in the figures and figure legends. We agree that including more donors for the HiC studies would increase the number of implicated variants and genes, however, all the chromatin-based V2G approaches described in our manuscript use relatively small sample sizes, but implicate more variants and genes than the comparable eQTL studies. I.e., the low overlap is not driven by a paucity of GWAS-chromatin-based associations. An alternative explanation for the low overlap between GWAS-chromatin-based approaches and eQTL approaches was recently by Pritchard and colleagues, who reported that GWAS and eQTL studies systematically implicate different types of variants (Mostafavi et al., Nature Genetics 2023). Among other differences, eQTL tend to implicate nearby genes while GWAS variants implicate distant genes, and our results support this contention. We referred to this study in the original version of the manuscript, but have included a more extensive discussion of potential explanations in the revised version. We thank the reviewer for helpful suggestions that have improved the quality of our study.

eLife assessment

This is a useful manuscript describing the competitive binding between Parkin domains to define the importance of dimerization in the mechanism of Parkin regulation and catalytic activity. The evidence supporting the importance of Parkin dimerization for an 'in trans' model of Parkin activity described in this manuscript is solid, but lacks more stringent and biochemical characterization of competitive binding that could provide more direct evidence to support the author's conclusions. This work will be of interest to those focused on defining the molecular mechanisms involved in ubiquitin ligase interactions, PINK-Parkin-mediated mitophagy, and mitochondrial organellar quality control.

Reviewer #1 (Public Review):

Summary:

The authors used structural and biophysical methods to provide insight into Parkin regulation. The breadth of data supporting their findings was impressive and generally well-orchestrated.

Strengths:

(1) They have done a better job explaining the rationale for their experiments thought-out.

(2) The use of molecular scissors in their construct represents a creative approach to examine inter-domain interactions. Appropriate controls were included.

(3) From my assessment, the experiments are well-conceived and executed.

(4) The authors do a better job of highlighting the question being addressed experimentally.

Reviewer #2 (Public Review):

In the revised manuscript, the authors tried to address some of my comments from the previous round of review. Notably, they have performed some additional ITC experiments where protein precipitation is not an issue to probe interactions between PARKIN and different domains. In addition, they have toned down some of the language in the text to better reflect their data and results. However, I still feel that the manuscript lacks some key answers regarding the relative interactions between p-PARKIN and different domains, as discussed in my previous review. A deeper dive into the underlying biophysical and biochemical features that drive these interactions is important to fully understand the importance of their work. However, this manuscript does provide some interesting potential insights into the mechanisms of PARKIN activation that could be useful for the field moving forward.

Reviewer #3 (Public Review):

Summary:

In their manuscript, Lenka et al present data that could suggest an "in trans" model of Parkin ubiquitination activity. Parkin is an intensely studied E3 ligase implicated in mitophagy, whereby missense mutations to the PARK2 gene are known to cause autosomal recessive juvenile parkinsonism. From a mechanistic point of view, Parkin is extremely complex. Its activity is tightly controlled by several modes of auto-inhibition that must be released by queues of mitochondrial damage. While the general overview of Parkin activation has been mapped out in recent years, several details have remained murky. In particular, whether Parkin dimerizes as part of its feed-forward signaling mechanism, and whether said dimerization can facilitate ligase activation, has remained unclear. Here, Lenka et al. use various truncation mutants of Parkin in an attempt to understand the likelihood of dimerization (in support of an "in trans" model for catalysis).

Strengths:

The results are bolstered by several distinct approaches including analytical SEC with cleavable Parkin constructs, ITC interaction studies, ubiquitination assays, protein crystallography, and cellular localization studies.

Weaknesses:

As presented, however, the storyline is very confusing to follow and several lines of experimentation felt like distractions from the primary message. Furthermore, many experiments could only indirectly support the author's conclusions, and therefore the final picture of what new features can be firmly added to the model of Parkin activation and function is unclear.

Following peer review and revision, the claims are still not fully supported by direct evidence. While the experimental system may be necessary and/or convenient given the unique challenges in studying Parkin, it does not directly speak toward the conclusions that the authors make, nor does it provide an accurate representation of biology.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The authors used structural and biophysical methods to provide insight into Parkin regulation. The breadth of data supporting their findings was impressive and generally well-orchestrated. Still, the impact of their results builds on recent structural studies and the stated impact is based on these prior works.

Strengths:

(1) After reading through the paper, the major findings are:

- RING2 and pUbl compete for binding to RING0.

- Parkin can dimerize.

- ACT plays an important role in enzyme kinetics.

(2) The use of molecular scissors in their construct represents a creative approach to examining inter-domain interactions.

(3) From my assessment, the experiments are well-conceived and executed.

We thank the reviewer for their positive remark and extremely helpful suggestions.

Weaknesses:

The manuscript, as written, is NOT for a general audience. Admittedly, I am not an expert on Parkin structure and function, but I had to do a lot of homework to try to understand the underlying rationale and impact. This reflects, I think, that the work generally represents an incremental advance on recent structural findings.

To this point, it is hard to understand the impact of this work without more information highlighting the novelty. There are several structures of Parkin in various auto-inhibited states, and it was hard to delineate how this is different.

For the sake of the general audience, we have included all the details of Parkin structures and conformations seen (Extended Fig. 1). The structures in the present study are to validate the biophysical/biochemical experiments, highlighting key findings. For example, we solved the phospho-Parkin (complex with pUb) structure after treatment with 3C protease (Fig. 2C), which washes off the pUbl-linker, as shown in Fig 2B. The structure of the pUbl-linker depleted phospho-Parkin-pUb complex showed that RING2 returned to the closed state (Fig. 2C), which is confirmation of the SEC assay in Fig. 2B. Similarly, the structure of the pUbl-linker depleted phospho-Parkin R163D/K211N-pUb complex (Fig. 3C), was done to validate the SEC data showing displacement of pUbl-linker is independent of pUbl interaction with the basic patch on RING0 (Fig. 3B). In addition, the latter structure also revealed a new donor ubiquitin binding pocket in the linker (connecting REP and RING2) region of Parkin (Fig. 9). Similarly, trans-complex structure of phospho-Parkin (Fig. 4D) was done to validate the biophysical data (Fig. 4A-C, Fig. 5A-D) showing trans-complex between phospho-Parkin and native Parkin. The latter also confirmed that the trans-complex was mediated by interactions between pUbl and the basic patch on RING0 (Fig. 4D). Furthermore, we noticed that the ACT region was disordered in the trans-complex between phospho-Parkin (1-140 + 141-382 + pUb) (Fig. 8A) which had ACT from the trans molecule, indicating ACT might be present in the cis molecule. The latter was validated from the structure of trans-complex between phospho-Parkin with cis ACT (1-76 + 77-382 + pUb) (Fig. 8C), showing the ordered ACT region. The structural finding was further validated by biochemical assays (Fig. 8 D-F, Extended Data Fig. 9C-E).

The structure of TEV-treated R0RBR (TEV) (Extended Data Fig. 4C) was done to ensure that the inclusion of TEV and treatment with TEV protease did not perturb Parkin folding, an important control for our biophysical experiments.

As noted, I appreciated the use of protease sites in the fusion protein construct. It is unclear how the loop region might affect the protein structure and function. The authors worked to demonstrate that this did not introduce artifacts, but the biological context is missing.

We thank the reviewer for appreciating the use of protease sites in the fusion protein construct.  Protease sites were used to overcome the competing mode of binding that makes interactions very transient and beyond the detection limit of methods such as ITC or SEC. While these interactions are quite transient in nature, they could still be useful for the activation of various Parkin isoforms that lack either the Ubl domain or RING2 domain (Extended Data Fig. 6, Fig. 10). Also, our Parkin localization assays also suggest an important role of these interactions in the recruitment of Parkin molecules to the damaged mitochondria (Fig. 6).

While it is likely that the binding is competitive between the Ubl and RING2 domains, the data is not quantitative. Is it known whether the folding of the distinct domains is independent? Or are there interactions that alter folding? It seems plausible that conformational rearrangements may invoke an orientation of domains that would be incompatible. The biological context for the importance of this interaction was not clear to me.

This is a great point. In the revised manuscript, we have included quantitative data between phospho-Parkin and untethered ∆Ubl-Parkin (TEV) (Fig. 5B) showing similar interactions using phospho-Parkin K211N and untethered ∆Ubl-Parkin (TEV) (Fig. 4B). Folding of Ubl domain or various combinations of RING domains lacking Ubl seems okay. Also, folding of the RING2 domain on its own appears to be fine. However, human Parkin lacking the RING2 domain seems to have some folding issues, majorly due to exposure of hydrophobic pocket on RING0, also suggested by previous efforts (Gladkova et al.ref. 24, Sauve et al. ref. 29).  The latter could be overcome by co-expression of RING2 lacking Parkin construct with PINK1 (Sauve et al. ref. 29) as phospho-Ubl binds on the same hydrophobic pocket on RING0 where RING2 binds. A drastic reduction in the melting temperature of phospho-Parkin (Gladkova et al.ref. 24), very likely due to exposure of hydrophobic surface between RING0 and RING2, correlates with the folding issues of RING0 exposed human Parkin constructs.

From the biological context, the competing nature between phospho-Ubl and RING2 domains could block the non-specific interaction of phosphorylated-ubiquitin-like proteins (phospho-Ub or phospho-NEDD8) with RING0 (Lenka et al. ref. 33), during Parkin activation. 

(5) What is the rationale for mutating Lys211 to Asn? Were other mutations tried? Glu? Ala? Just missing the rationale. I think this may have been identified previously in the field, but not clear what this mutation represents biologically.

Lys211Asn is a Parkinson’s disease mutation; therefore, we decided to use the same mutation for biophysical studies.  

I was confused about how the phospho-proteins were generated. After looking through the methods, there appear to be phosphorylation experiments, but it is unclear what the efficiency was for each protein (i.e. what % gets modified). In the text, the authors refer to phospho-Parkin (T270R, C431A), but not clear how these mutations might influence this process. I gather that these are catalytically inactive, but it is unclear to me how this is catalyzing the ubiquitination in the assay.

This is an excellent question. Because different phosphorylation statuses would affect the analysis, we ensured complete phosphorylation status using Phos-Tag SDS-PAGE, as shown below.

Author response image 1.

Our biophysical experiments in Fig. 5C show that trans complex formation is mediated by interactions between the basic patch (comprising K161, R163, K211) on RING0 and phospho-Ubl domain in trans. These interactions result in the displacement of RING2 (Fig. 5C). Parkin activation is mediated by displacement of RING2 and exposure of catalytic C431 on RING2. While phospho-Parkin T270R/C431A is catalytically dead, the phospho-Ubl domain of phospho-Parkin T270R/C431would bind to the basic patch on RING0 of WT-Parkin resulting in activation of WT-Parkin as shown in Fig. 5E. A schematic figure is shown below to explain the same.

Author response image 2.

(7) The authors note that "ACT can be complemented in trans; however, it is more efficient in cis", but it is unclear whether both would be important or if the favored interaction is dominant in a biological context.

First, this is an excellent question about the biological context of ACT and needs further exploration. While due to the flexible nature of ACT, it can be complemented both in cis and trans, we can only speculate cis interactions between ACT and RING0 could be more relevant from the biological context as during protein synthesis and folding, ACT would be translated before RING2, and thus ACT would occupy the small hydrophobic patch on RING0 in cis. Unpublished data shows the replacement of the ACT region by Biogen compounds to activate Parkin (https://doi.org/10.21203/rs.3.rs-4119143/v1). The latter finding further suggests the flexibility in this region.        

(8) The authors repeatedly note that this study could aid in the development of small-molecule regulators against Parkin to treat PD, but this is a long way off. And it is not clear from their manuscript how this would be achieved. As stated, this is conjecture.

As suggested by this reviewer, we have removed this point in the revised manuscript.

Reviewer #2 (Public Review):

This manuscript uses biochemistry and X-ray crystallography to further probe the molecular mechanism of Parkin regulation and activation. Using a construct that incorporates cleavage sites between different Parkin domains to increase the local concentration of specific domains (i.e., molecular scissors), the authors suggest that competitive binding between the p-Ubl and RING2 domains for the RING0 domain regulates Parkin activity. Further, they demonstrate that this competition can occur in trans, with a p-Ubl domain of one Parkin molecule binding the RING0 domain of a second monomer, thus activating the catalytic RING1 domain. In addition, they suggest that the ACT domain can similarly bind and activate Parkin in trans, albeit at a lower efficiency than that observed for p-Ubl. The authors also suggest from crystal structure analysis and some biochemical experiments that the linker region between RING2 and repressor elements interacts with the donor ubiquitin to enhance Parkin activity.<br /> Ultimately this manuscript challenges previous work suggesting that the p-Ubl domain does not bind to the Parkin core in the mechanism of Parkin activation. The use of the 'molecular scissors' approach to probe these effects is an interesting approach to probe this type of competitive binding. However, there are issues with the experimental approach manuscript that detract from the overall quality and potential impact of the work.

We thank the reviewer for their positive remark and constructive suggestions.

The competitive binding between p-Ubl and RING2 domains for the Parkin core could have been better defined using biophysical and biochemical approaches that explicitly define the relative affinities that dictate these interactions. A better understanding of these affinities could provide more insight into the relative bindings of these domains, especially as it relates to the in trans interactions.

This is an excellent point regarding the relative affinities of pUbl and RING2 for the Parkin core (lacking Ubl and RING2). While we could purify p-Ubl, we failed to purify human Parkin (lacking RING2 and phospho-Ubl). The latter folding issues were likely due to the exposure of a highly hydrophobic surface on RING0 (as shown below) in the absence of pUbl and RING2 in the R0RB construct. Also, RING2 with an exposed hydrophobic surface would be prone to folding issues, which is not suitable for affinity measurements. A drastic reduction in the melting temperature of phospho-Parkin (Gladkova et al.ref. 24) also highlights the importance of a hydrophobic surface between RING0 and RING2 on Parkin folding/stability. A separate study would be required to try these Parkin constructs from different species and ensure proper folding before using them for affinity measurements.

Author response image 3.

I also have concerns about the results of using molecular scissors to 'increase local concentrations' and allow for binding to be observed. These experiments are done primarily using proteolytic cleavage of different domains followed by size exclusion chromatography. ITC experiments suggest that the binding constants for these interactions are in the µM range, although these experiments are problematic as the authors indicate in the text that protein precipitation was observed during these experiments. This type of binding could easily be measured in other assays. My issue relates to the ability of a protein complex (comprising the core and cleaved domains) with a Kd of 1 µM to be maintained in an SEC experiment. The off-rates for these complexes must be exceeding slow, which doesn't really correspond to the low µM binding constants discussed in the text. How do the authors explain this? What is driving the Koff to levels sufficiently slow to prevent dissociation by SEC? Considering that the authors are challenging previous work describing the lack of binding between the p-Ubl domain and the core, these issues should be better resolved in this current manuscript. Further, it's important to have a more detailed understanding of relative affinities when considering the functional implications of this competition in the context of full-length Parkin. Similar comments could be made about the ACT experiments described in the text.

This is a great point. In the revised manuscript, we repeated ITC measurements in a different buffer system, which gave nice ITC data. In the revised manuscript, we have also performed ITC measurements using native phospho-Parkin. Phospho-Parkin and untethered ∆Ubl-Parkin (TEV) (Fig. 5B) show similar affinities as seen between phospho-Parkin K211N and untethered ∆Ubl-Parkin (TEV) (Fig. 4B). However, Kd values were consistent in the range of 1.0 ± 0.4 µM which could not address the reviewer’s point regarding slow off-rate. The crystal structure of the trans-complex of phospho-Parkin shows several hydrophobic and ionic interactions between p-Ubl and Parkin core, suggesting a strong interaction and, thus, justifying the co-elution on SEC. Additionally, ITC measurements between E2-Ub and P-Parkin-pUb show similar affinity (Kd = 0.9 ± 0.2 µM) (Kumar et al., 2015, EMBO J.), and yet they co-elute on SEC (Kumar et al., 2015, EMBO J.).

Ultimately, this work does suggest additional insights into the mechanism of Parkin activation that could contribute to the field. There is a lot of information included in this manuscript, giving it breadth, albeit at the cost of depth for the study of specific interactions. Further, I felt that the authors oversold some of their data in the text, and I'd recommend being a bit more careful when claiming an experiment 'confirms' a specific model. In many cases, there are other models that could explain similar results. For example, in Figure 1C, the authors state that their crystal structure 'confirms' that "RING2 is transiently displaced from the RING0 domain and returns to its original position after washing off the p-Ubl linker". However, it isn't clear to me that RING2 ever dissociated when prepared this way. While there are issues with the work that I feel should be further addressed with additional experiments, there are interesting mechanistic details suggested by this work that could improve our understanding of Parkin activation. However, the full impact of this work won't be fully appreciated until there is a more thorough understanding of the regulation and competitive binding between p-Ubl and RIGN2 to RORB both in cis and in trans.

We thank the reviewer for their positive comment. In the revised manuscript, we have included the reviewer’s suggestion. The conformational changes in phospho-Parkin were established from the SEC assay (Fig. 2A and Fig. 2B), which show displacement/association of phospho-Ubl or RING2 after treatment of phospho-Parkin with 3C and TEV, respectively. For crystallization, we first phosphorylated Parkin, where RING2 is displaced due to phospho-Ubl (as shown in SEC), followed by treatment with 3C protease, which led to pUbl wash-off. The Parkin core separated from phospho-Ubl on SEC was used for crystallization and structure determination in Fig. 2C, where RING2 returned to the RING0 pocket, which confirms SEC data (Fig. 2B).

Reviewer #3 (Public Review):

Summary:

In their manuscript "Additional feedforward mechanism of Parkin activation via binding of phospho-UBL and RING0 in trans", Lenka et al present data that could suggest an "in trans" model of Parkin ubiquitination activity. Parkin is an intensely studied E3 ligase implicated in mitophagy, whereby missense mutations to the PARK2 gene are known to cause autosomal recessive juvenile parkinsonism. From a mechanistic point of view, Parkin is extremely complex. Its activity is tightly controlled by several modes of auto-inhibition that must be released by queues of mitochondrial damage. While the general overview of Parkin activation has been mapped out in recent years, several details have remained murky. In particular, whether Parkin dimerizes as part of its feed-forward signaling mechanism, and whether said dimerization can facilitate ligase activation, has remained unclear. Here, Lenka et al. use various truncation mutants of Parkin in an attempt to understand the likelihood of dimerization (in support of an "in trans" model for catalysis).

Strengths:

The results are bolstered by several distinct approaches including analytical SEC with cleavable Parkin constructs, ITC interaction studies, ubiquitination assays, protein crystallography, and cellular localization studies.

We thank the reviewer for their positive remark.

Weaknesses:

As presented, however, the storyline is very confusing to follow and several lines of experimentation felt like distractions from the primary message. Furthermore, many experiments could only indirectly support the author's conclusions, and therefore the final picture of what new features can be firmly added to the model of Parkin activation and function is unclear.

We thank the reviewer for their constructive criticism, which has helped us to improve the quality of this manuscript.

Major concerns:

(1) This manuscript solves numerous crystal structures of various Parkin components to help support their idea of in trans transfer. The way these structures are presented more resemble models and it is unclear from the figures that these are new complexes solved in this work, and what new insights can be gleaned from them.

The structures in the present study are to validate the biophysical/biochemical experiments highlighting key findings. For example, we solved the phospho-Parkin (complex with pUb) structure after treatment with 3C protease (Fig. 2C), which washes off the pUbl-linker, as shown in Fig. 2B. The structure of pUbl-linker depleted phospho-Parkin-pUb complex showed that RING2 returned to the closed state (Fig. 2C), which is confirmation of the SEC assay in Fig. 2B. Similarly, the structure of the pUbl-linker depleted phospho-Parkin R163D/K211N-pUb complex (Fig. 3C), was done to validate the SEC data showing displacement of pUbl-linker is independent of pUbl interaction with the basic patch on RING0 (Fig. 3B). In addition, the latter structure also revealed a new donor ubiquitin binding pocket in the linker (connecting REP and RING2) region of Parkin (Fig. 9). Similarly, trans-complex structure of phospho-Parkin (Fig. 4D) was done to validate the biophysical data (Fig. 4A-C, Fig. 5A-D) showing trans-complex between phospho-Parkin and native Parkin. The latter also confirmed that the trans-complex was mediated by interactions between pUbl and the basic patch on RING0 (Fig. 4D). Furthermore, we noticed that the ACT region was disordered in the trans-complex between phospho-Parkin (1-140 + 141-382 + pUb) (Fig. 8A) which had ACT from the trans molecule, indicating ACT might be present in the cis molecule. The latter was validated from the structure of trans-complex between phospho-Parkin with cis ACT (1-76 + 77-382 + pUb) (Fig. 8C), showing the ordered ACT region. The structural finding was further validated by biochemical assays (Fig. 8 D-F, Extended Data Fig. 9C-E).

The structure of TEV-treated R0RBR (TEV) (Extended Data Fig. 4C) was done to ensure that the inclusion of TEV and treatment with TEV protease did not perturb Parkin folding, an important control for our biophysical experiments.

(2) There are no experiments that definitively show the in trans activation of Parkin. The binding experiments and size exclusion chromatography are a good start, but the way these experiments are performed, they'd be better suited as support for a stronger experiment showing Parkin dimerization. In addition, the rationale for an in trans activation model is not convincingly explained until the concept of Parkin isoforms is introduced in the Discussion. The authors should consider expanding this concept into other parts of the manuscript.

We thank the reviewer for appreciating the Parkin dimerization. Our biophysical data in Fig. 5C shows that Parkin dimerization is mediated by interactions between phospho-Ubl and RING0 in trans, leading to the displacement of RING2. However, Parkin K211N (on RING0) mutation perturbs interaction with phospho-Parkin and leads to loss of Parkin dimerization and loss of RING2 displacement (Fig. 5C). The interaction between pUbl and K211 pocket on RING0 leads to the displacement of RING2 resulting in Parkin activation as catalytic residue C431 on RING2 is exposed for catalysis. The biophysical experiment is further confirmed by a biochemical experiment where the addition of catalytically in-active phospho-Parkin T270R/C431A activates autoinhibited WT-Parkin in trans using the mechanism as discussed (a schematic representation also shown in Author response image 2).

We thank this reviewer regarding Parkin isoforms. In the revised manuscript, we have included Parkin isoforms in the results section, too.

(2a) For the in trans activation experiment using wt Parkin and pParkin (T270R/C431A) (Figure 3D), there needs to be a large excess of pParkin to stimulate the catalytic activity of wt Parkin. This experiment has low cellular relevance as these point mutations are unlikely to occur together to create this nonfunctional pParkin protein. In the case of pParkin activating wt Parkin (regardless of artificial point mutations inserted to study specifically the in trans activation), if there needs to be much more pParkin around to fully activate wt Parkin, isn't it just more likely that the pParkin would activate in cis?

To test phospho-Parkin as an activator of Parkin in trans, we wanted to use the catalytically inactive version of phospho-Parkin to avoid the background activity of p-Parkin. While it is true that a large excess of pParkin (T270R/C431A) is required to activate WT-Parkin in the in vitro set-up, it is not very surprising as in WT-Parkin, the unphosphorylated Ubl domain would block the E2 binding site on RING1. Also, due to interactions between pParkin (T270R/C431A) molecules, the net concentration of pParkin (T270R/C431A) as an activator would be much lower. However, the Ubl blocking E2 binding site on RING1 won’t be an issue between phospho-Parkin molecules or between Parkin isoforms (lacking Ubl domain or RING2).

(2ai) Another underlying issue with this experiment is that the authors do not consider the possibility that the increased activity observed is a result of increased "substrate" for auto-ubiquitination, as opposed to any role in catalytic activation. Have the authors considered looking at Miro as a substrate in order to control for this?

This is quite an interesting point. However, this will be only possible if Parkin is ubiquitinated in trans, as auto-ubiquitination is possible with active Parkin and not with catalytically dead (phospho-Parkin T270R, C431A) or autoinhibited (WT-Parkin). Also, in the previous version of the manuscript, where we used only phospho-Ubl as an activator of Parkin in trans, we tested Miro1 ubiquitination and auto-ubiquitination, and the results were the same (Author response image 4).

Author response image 4.

(2b) The authors mention a "higher net concentration" of the "fused domains" with RING0, and use this to justify artificially cleaving the Ubl or RING2 domains from the Parkin core. This fact should be moot. In cells, it is expected there will only be a 1:1 ratio of the Parkin core with the Ubl or RING2 domains. To date, there is no evidence suggesting multiple pUbls or multiple RING2s can bind the RING0 binding site. In fact, the authors here even show that either the RING2 or pUbl needs to be displaced to permit the binding of the other domain. That being said, there would be no "higher net concentration" because there would always be the same molar equivalents of Ubl, RING2, and the Parkin core.

We apologize for the confusion. “Higher net concentration” is with respect to fused domains versus the domain provided in trans. Due to the competing nature of the interactions between pUbl/RING2 and RING0, the interactions are too transient and beyond the detection limit of the biophysical techniques. While the domains are fused (for example, RING0-RING2 in the same polypeptide) in a polypeptide, their effective concentrations are much higher than those (for example, pUbl) provided in trans; thus, biophysical methods fail to detect the interaction. Treatment with protease solves the above issue due to the higher net concentration of the fused domain, and trans interactions can be measured using biophysical techniques. However, the nature of these interactions and conformational changes is very transient, which is also suggested by the data. Therefore, Parkin molecules will never remain associated; rather, Parkin will transiently interact and activate Parkin molecules in trans.

(2c) A larger issue remaining in terms of Parkin activation is the lack of clarity surrounding the role of the linker (77-140); particularly whether its primary role is to tether the Ubl to the cis Parkin molecule versus a role in permitting distal interactions to a trans molecule. The way the authors have conducted the experiments presented in Figure 2 limits the possible interactions that the activated pUbl could have by (a) ablating the binding site in the cis molecule with the K211N mutation; (b) further blocking the binding site in the cis molecule by keeping the RING2 domain intact. These restrictions to the cis parkin molecule effectively force the pUbl to bind in trans. A competition experiment to demonstrate the likelihood of cis or trans activation in direct comparison with each other would provide stronger evidence for trans activation.

This is an excellent point. In the revised manuscript, we have performed experiments using native phospho-Parkin (Revised Figure 5), and the results are consistent with those in Figure 2 ( Revised Figure 4), where we used the K211N mutation.

(3) A major limitation of this study is that the authors interpret structural flexibility from experiments that do not report directly on flexibility. The analytical SEC experiments report on binding affinity and more specifically off-rates. By removing the interdomain linkages, the accompanying on-rate would be drastically impacted, and thus the observations are disconnected from a native scenario. Likewise, observations from protein crystallography can be consistent with flexibility, but certainly should not be directly interpreted in this manner. Rigorous determination of linker and/or domain flexibility would require alternative methods that measure this directly.

We also agree with the reviewer that these methods do not directly capture structural flexibility. Also, rigorous determination of linker flexibility would require alternative methods that measure this directly. However, due to the complex nature of interactions and technical limitations, breaking the interdomain linkages was the best possible way to capture interactions in trans. Interestingly, all previous methods that report cis interactions between pUbl and RING0 also used a similar approach (Gladkova et al.ref. 24, Sauve et al. ref. 29).  

(4) The analysis of the ACT element comes across as incomplete. The authors make a point of a competing interaction with Lys48 of the Ubl domain, but the significance of this is unclear. It is possible that this observation could be an overinterpretation of the crystal structures. Additionally, the rationale for why the ACT element should or shouldn't contribute to in trans activation of different Parkin constructs is not clear. Lastly, the conclusion that this work explains the evolutionary nature of this element in chordates is highly overstated.

We agree with the reviewer that the significance of Lys48 is unclear. We have presented this just as one of the observations from the crystal structure. As the reviewer suggested, we have removed the sentence about the evolutionary nature of this element from the revised manuscript.

(5) The analysis of the REP linker element also seems incomplete. The authors identify contacts to a neighboring pUb molecule in their crystal structure, but the connection between this interface (which could be a crystallization artifact) and their biochemical activity data is not straightforward. The analysis of flexibility within this region using crystallographic and AlphaFold modeling observations is very indirect. The authors also draw parallels with linker regions in other RBR ligases that are involved in recognizing the E2-loaded Ub. Firstly, it is not clear from the text or figures whether the "conserved" hydrophobic within the linker region is involved in these alternative Ub interfaces. And secondly, the authors appear to jump to the conclusion that the Parkin linker region also binds an E2-loaded Ub, even though their original observation from the crystal structure seems inconsistent with this. The entire analysis feels very preliminary and also comes across as tangential to the primary storyline of in trans Parkin activation.

We agree with the reviewer that crystal structure data and biochemical data are not directly linked. In the revised manuscript, we have also highlighted the conserved hydrophobic in the linker region at the ubiquitin interface (Fig. 9C and Extended Data Fig. 11A), which was somehow missed in the original manuscript. We want to add that a very similar analysis and supporting experiments identified donor ubiquitin-binding sites on the IBR and helix connecting RING1-IBR (Kumar et al., Nature Str. and Mol. Biol., 2017), which several other groups later confirmed. In the mentioned study, the Ubl domain of Parkin from the symmetry mate Parkin molecule was identified as a mimic of “donor ubiquitin” on IBR and helix connecting RING1-IBR.

In the present study, a neighboring pUb molecule in the crystal structure is identified as a donor ubiquitin mimic (Fig. 9C) by supporting biophysical/biochemical experiments. First, we show that mutation of I411A in the REP linker of Parkin perturbs Parkin interaction with E2~Ub (donor) (Fig. 9F). Another supporting experiment was performed using a Ubiquitin-VS probe assay, which is independent of E2. Assays using Ubiquitin-VS show that I411A mutation in the REP-RING2 linker perturbs Parkin charging with Ubiquitin-VS (Extended Data Fig. 11 B). Furthermore, the biophysical data showing loss of Parkin interaction with donor ubiquitin is further supported by ubiquitination assays. Mutations in the REP-RING2 linker perturb the Parkin activity (Fig. 9E), confirming biophysical data. This is further confirmed by mutations (L71A or L73A) on ubiquitin (Extended Data Fig. 11C), resulting in loss of Parkin activity. The above experiments nicely establish the role of the REP-RING2 linker in interaction with donor ubiquitin, which is consistent with other RBRs (Extended Data Fig. 11A).

While we agree with the reviewer that this appears tangential to the primary storyline in trans-Parkin activation, we decided to include this data because it could be of interest to the field.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) For clarity, a schematic of the domain architecture of Parkin would be helpful at the outset in the main figures. This will help with the introduction to better understand the protein organization. This is lost in the Extended Figure in my opinion.

We thank the reviewer for suggesting this, which we have included in Figure 1 of the revised manuscript.

(2) Related to the competition between the Ubl and RING2 domains, can competition be shown through another method? SPR, ITC, etc? ITC was used in other experiments, but only in the context of mutations (Lys211Asn)? Can this be done with WT sequence?

This is an excellent suggestion. In the revised Figure 5, we have performed ITC experiment using WT Parkin, and the results are consistent with what we observed using Lys211Asn Parkin.

(3) The authors also note that "the AlphaFold model shows a helical structure in the linker region of Parkin (Extended Data Figure 10C), further confirming the flexible nature of this region"... but the secondary structure would not be inherently flexible. This is confusing.

The flexibility is in terms of the conformation of this linker region observed under the open or closed state of Parkin. In the revised manuscript, we have explained this point more clearly.

(4) The manuscript needs extensive revision to improve its readability. Minor grammatical mistakes were prevalent throughout.

We thank the reviewer for pointing out this and we have corrected these in the revised manuscript.

(5) The confocal images are nice, but inset panels may help highlight the regions of interest (ROIs).

This is corrected in the revised manuscript.

(6) Trans is misspelled ("tans") towards the end of the second paragraph on page 16.

This is corrected in the revised manuscript.

(7) The schematics are helpful, but some of the lettering in Figure 2 is very small.

This is corrected in the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

(1) A significant portion of the results section refers to the supplement, making the overall readability very difficult.

We accept this issue as a lot of relevant data could not be added to the main figures and thus ended up in the supplement.  In the revised manuscript, we have moved some of the supplementary figures to the main figures.

(2) Interpretation of the experiments utilizing many different Parkin constructs and cleavage scenarios (particularly the SEC and crystallography experiments) is extremely difficult. The work would benefit from a layout of the Parkin model system, highlighting cleavage sites, key domain terminology, and mutations used in the study, presented together and early on in the manuscript. Using this to identify a simpler system of referencing Parkin constructs would also be a large improvement.

This is a great suggestion. We have included these points in the revised manuscript, which has improved the readability.

(3) Lines 81-83; the authors say they "demonstrate the conformational changes in Parkin during the activation process", but fail to show any actual conformational changes. Further, much of what is demonstrated in this work (in terms of crystal structures) corroborates existing literature. The authors should use caution not to overstate their original conclusions in light of the large body of work in this area.

We thank the reviewer for pointing out this. We have corrected the above statement in the revised manuscript to indicate that we meant it in the context of trans conformational changes.

(4) Line 446 and 434; there is a discrepancy about which amino acid is present at residue 409. Is this a K408 typo? The authors also present mutational work on K416, but this residue is not shown in the structure panel.

We thank the reviewer for pointing out this. In the revised manuscript, we have corrected these typos.

eLife assessment

This study presents important findings on the different polymorphs of alpha-synuclein filaments that form at various pH's during in vitro assembly reactions with purified recombinant protein. Of particular note is the discovery of two new polymorphs (1M and 5A) that form in PBS buffer at pH 7. The strength of the evidence presented is convincing. The work will be of interest to biochemists and biophysicists working on protein aggregation and amyloids.

Reviewer #2 (Public Review):

Summary:

This is an exciting paper that explores the in vitro assembly of recombinant alpha-synuclein into amyloid filaments. The authors changed the pH and the composition of the assembly buffers, as well as the presence of different types of seeds, and analysed the resulting structures by cryo-EM.

Strengths:

By doing experiments at different pHs, the authors found that so-called type 2 and type-3 polymorphs form in a pH dependent manner. In addition, they find that type-1 filaments form in the presence of phosphate ions. One of their in vitro assembled type-1 polymorphs is similar to the alpha-synuclein filaments that were extracted from the brain of an individual with juvenile-onset synucleinopathy (JOS). They hypothesize that additional densities in a similar place as additional densities in the JOS fold correspond to phosphate ions.

Comments on the revised version:

This is OK now. I thank the authors for their constructive engagement with my comments.

Reviewer #3 (Public Review):

Summary

The high heterogeneity nature of α-synuclein (α-syn) fibrils posed significant challenges in structural reconstruction of the ex vivo conformation. A deeper understanding of the factors influencing the formation of various α-syn polymorphs remains elusive. The manuscript by Frey et al. provides a comprehensive exploration of how pH variations (ranging from 5.8 to 7.4) affect the selection of α-syn polymorphs (specifically, Type1, 2 and 3) in vitro by using cryo-electron microscopy (cryo-EM) and helical reconstruction techniques. Crucially, the authors identify two novel polymorphs at pH 7.0 in PBS. These polymorphs bear resemblance to the structure of patient-derived juvenile-onset synucleinopathy (JOS) polymorph and diseased tissue amplified α-syn fibrils. The revised manuscript more strongly supports the notion that seeding is a non-polymorph-specific in the context of secondary nucleation-dominated aggregation, underscoring the irreplaceable role of pH in polymorph formation.

Strengths

This study systematically investigates the effects of environmental conditions and seeding on the structure of α-syn fibrils. It emphasizes the significant influence of environmental factors, especially pH, in determining the selection of α-syn polymorphs. The high-resolution structures obtained through cryo-EM enable a clear characterization of the composition and proportion of each polymorph in the sample. Collectively, this work provides a strong support for the pronounced sensitivity of α-syn fibril structures to the environmental conditions and systematically categorizes previously reported α-syn fibril structures. Furthermore, the identification of JOS-like polymorph also demonstrates the possibility of in vitro reconstruction of brain-derived α-syn fibril structures.

Weaknesses

All my previous concerns have been resolved to my satisfaction.

Author response:

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

Revisions Round 1

Reviewer #1

We thank the reviewer for their careful reading of our manuscript and have taken all of their grammatical corrections into account.

Reviewer #2 (Public Review): 

Weaknesses: 

The paper contains multiple instances of non-scientific language, as indicated below. It would also benefit from additional details on the cryo-EM structure determination in the Methods and inclusion of commonly accepted requirements for cryo-EM structures, like examples of 2D class averages, raw micrographs, and FSC curves (between half-maps as well as between rigid-body fitted (or refined) atomic models of the different polymorphs and their corresponding maps). In addition, cryo-EM maps for the control experiments F1 and F2 should be presented in Figure 9.

We tried to correct the non-scientific language and have included the suggested data on the Cryo-EM analyses including new Figures 11-17.  We did not collect data on the sample used for the seeds in the cross seeding experiments because we had already confirmed in multiple datasets that the conditions in F1 and F2 reproducibly produce fibrils of Type 1 and Type 3, respectively. We have now analyzed cryo-EM data for 6 more samples at pH 7.0 and found that several kinds of polymorphs (Types 1A, 1M, 2A, 2B and 5) are accessible at this pH, however the Type 3 polymorphs are not formed at pH 7.0 under the conditions that we used for aggregation.

Reviewer #2 (Recommendations For The Authors): 

- remove unscientific language: "it seems that there are about as many unique atomic-resolution structures of these aggregates as there are publications describing them"   

We have rephrased this sentence.

- for same reason, remove "Obviously, " 

Done

- What does this mean? “polymorph-unspecific” 

Rephrased as non-polymorph-specific

- What does this mean? "shallow amyloid energy hypersurface"  

By “shallow hypersurface” we mean that the minimum of the multi-dimensional function that describes the energy of the amyloid is not so deep that subtle changes to the environment will not favor another fold/energy minimum. We have left the sentence because while it may not be perfect, it is concise and seems to get the point across.

- "The results also confirm the possibility of producing disease-relevant structure in vitro." -> This is incorrect as no disease-relevant structure was replicated in this work. Use another word like “suggest”.

We have changed to “suggest” as suggested.

- Remove "historically" 

Done

- Rephrase “It has long been understood that all amyloids contain a common structural scaffold” 

Changed to “It has long been established that all amyloids contain a common structural scaffold..” 

- "Amyloid polymorphs whose differences lie in both their tertiary structure (the arrangement of the beta-strands) and the quaternary structure (protofilamentprotofilament assembly) have been found to display distinct biological activities [8]" -> I don't think this is true, different biological activities of amyloids have never been linked to their distinct structures.  

We have added 5 new references (8-12) to support this sentence.

- Reference 10 is a comment on reference 9; it should be removed. Instead, as for alpha-synuclein, all papers describing the tau structures should be included.  

We have removed the reference, but feel that the addition of all Tau structure references is not merited in this manuscript since we are not comparing them.

- Rephrase: "is not always 100% faithful"

Removed “100%”

- What is pseudo-C2 symmetry? Do the authors mean pseudo 2_1 symmetry (ie a 2-start helical symmetry)?

Thank for pointing this out.  We did indeed mean pseudo 21 helical symmetry.  

- Re-phrase: "alpha-Syn's chameleon-like behavior" 

We have removed this phrase.

- "In the case of alpha-Syn, the secondary nucleation mechanism is based on the interaction of the positively charged N-terminal region of monomeric alpha-Syn and the disordered, negatively charged C-terminal region of the alpha-Syn amyloid fibrils [54]" -> I would say the mechanisms of secondary nucleation are not that well understood yet, so one may want to tune this down a bit. 

We have changed this to “mechanism has been proposed to be”

- The paragraphs describing experiments by others are better suited for a Discussion rather than a Results section. Perhaps re-organize this part? 

We have left the text intact as we are using a Results and Discussion format.

- A lot of information about Image processing seems to be missing: what steps were performed after initial model generation? 

We have added more details in the methods section on the EM data processing and model analysis.

- Figure 1: Where is Type 4 on the pH scale?

We have adjusted the Fig 1 legend to clarify that pH scale is only applicable to the structures presented in this manuscript. 

- Figure 2: This might be better incorporated as a subpanel of Figure 1.

We agree that this figure is somewhat of a loner on its own and we only added it in order to avoid confusion with the somewhat inconsistent naming scheme used for the Type 1B structure. However, we prefer to leave it as a separate figure so that it does not get dilute the impact of figure 1.

- Figure 3: What is the extra density at the bottom of Type 3B from pH 5.8 samples 1 and 2. pH 5.8 + 50mM NaCl (but not pH 5.8 + 100 mM NaCl)? Could this be an indication of a local minimum and the pH 5.8 + 100 mM NaCl structure is correct? Or is this a real difference between 0/50mM NaCl and 100 mM NaCl? 

We did not see the extra density to which the reviewer is referring, however the images used in this panel are the based on the output of 3D-classification which is more likely to produce more artifacts than a 3D refinement. With this in mind, we did not see any significant differences in the refined structures and therefore only deposited the better quality map and model for each of the polymorph types.

- Figure 3: To what extent is Type 3B of pH 6.5 still a mixture of different types? The density looks poor. In general, in the absence of more details about the cryo-EM maps, it is hard to assess the quality of the structures presented.  

In order to improve the quality of the images in this panel, a more complete separation of the particles from each polymorph was achieved via the filament subset selection tool in RELION 5. In each case, an unbiased could be created from the 2D classes via the relion_helix_inimodel2D program, further supporting the coexistence of 4 polymorphs in the pH 6.5 sample. The particles were individually refined to produce the respective maps that are now used in this figure.

- Many references are incorrect, containing "Preprint at (20xx)" statements.

This has been corrected.  

Reviewer #3 (Public Review): 

Weaknesses: 

(1) The authors reveal that both Type 1 monofilament fibril polymorph (reminiscent of JOSlike polymorph) and Type 5 polymorph (akin to tissue-amplified-like polymorph) can both form under the same condition. Additionally, this condition also fosters the formation of flat ribbon-like fibril across different batches. Notably, at pH 5.8, variations in experimental groups yield disparate abundance ratios between polymorph 3B and 3C, indicating a degree of instability in fibrillar formation. The variability would potentially pose challenges for replicability in subsequent research. In light of these situations, I propose the following recommendations: 

(a) An explicit elucidation of the factors contributing to these divergent outcomes under similar experimental conditions is warranted. This should include an exploration of whether variations in purified protein batches are contributing factors to the observed heterogeneity.

We are in complete agreement that understanding the factors that lead to polymorph variability is of utmost importance (and was the impetus for the manuscript itself). However the number of variables to explore is overwhelming and we will continue to investigate this in our future research. Regarding the variability between batches of purified protein, we also think that this could be a factor in the polymorph variability observed for otherwise “identical” aggregation conditions, particularly at pH 7 where the largest variety of polymorphs have been observed. However, even variation between identical replicates (samples created from the same protein solution and simply aggregated simultaneously in separate tubes) can lead to different outcomes (see datasets 15 and 16 in the revised Table 1) suggesting that there are stochastic processes that can determine the outcome of an individual aggregation experiment. While our data still indicates that Type 1,2 and 3 polymorphs are strongly selected by pH, the selection between interface variants 3B vs. 3C and 2A vs. 2B might also be affected by protein purity. Our standard purification protocol produces a single band by coomassie-stained SDS-PAGE however minor truncations and other impurities below a few percent would go undetected and, given the proposed roles of the N and C-termini in secondary nucleation, could have a large effect on polymorph selection and seeding. In line with the reviewer’s comments we now include a batch number for each EM dataset. While no new conclusions can be drawn from the inclusion of this additional data, we feel that it is important to acknowledge the possible role of batch to batch variability. 

(b) To enhance the robustness of the conclusions, additional replicates of the experiments under the same condition should be conducted, ideally a minimum of three times.  

The pH 5.8 conditions that yield Type 3 fibrils has already been repeated several times in the original manuscript. Since the pH 7.4 conditions produce the most common a-Syn polymorph (Type 1A) and were produced twice in this manuscript (once as an unseeded and once as a cross-seeded fibrilization) we decided to focus on the intermediate condition where the most variability had been seen (pH 7.0). The revised table 1 now has 6 new datasets (11-16) representing 6 independent aggregations at pH 7.0 starting from two different protein purification batches. The results is that we now produce the type 2A/B polymorphs in three samples and in two of these samples we once again observed the type 1M polymorph.  The other samples produced Type 1A or non-twisted fibrils.

(c) Further investigation into whether different polymorphs formed under the same buffer condition could lead to distinct toxicological and pathology effects would be a valuable addition to the study.  

The correlation of toxicity with structure would in principle be interesting. However the Type 1 and Type 3 polymorphs formed at pH 5.8 and 7.4 are not likely to be biologically relevant. The pH 7 polymorphs (Type 5 and 1M) would be more interesting because they form under the same conditions and might be related to some disease relevant structures. Still, it is rare that a single polymorph appears at 7.0 (the Type 5 represented only 10-20% of the fibrils in the sample and the Type 1M also had unidentified double-filament fibrils in the sample). We plan to pursue this line of research and hope to include it in a future publication.

(2) The cross-seeding study presented in the manuscript demonstrates the pivotal role of pH conditions in dictating conformation. However, an intriguing aspect that emerges is the potential role of seed concentration in determining the resultant product structure. This raises a critical question: at what specific seed concentration does the determining factor for polymorph selection shift from pH condition to seed concentration? A methodological robust approach to address this should be conducted through a series of experiments across a range of seed concentrations. Such an approach could delineate a clear boundary at which seed concentration begins to predominantly dictate the conformation, as opposed to pH conditions. Incorporating this aspect into the study would not only clarify the interplay between seed concentration and pH conditions, but also add a fascinating dimension to the understanding of polymorph selection mechanisms.

A more complete analysis of the mechanisms of aggregation, including the effect of seed concentration and the resulting polymorph specificity of the process, are all very important for our understanding of the aggregation pathways of alpha-synuclein and are currently the topic of ongoing investigations in our lab.

Furthermore, the study prompts additional queries regarding the behavior of cross-seeding production under the same pH conditions when employing seeds of distinct conformation. Evidence from various studies, such as those involving E46K and G51D cross-seeding, suggests that seed structure plays a crucial role in dictating polymorph selection. A key question is whether these products consistently mirror the structure of their respective seeds. 

We thank the reviewer for reminding us to cite these studies as a clear example of polymorph selection by cross-seeding. Unfortunately, it is not 100% clear from the G51D cross seeding manuscript (https://doi.org/10.1038/s41467-021-26433-2) what conditions were used in the cross-seeding since different conditions were used for the seedless wild-type and mutant aggregations… however it appears that the wildtype without seeds was Tris pH 7.5 (although at 37C the pH could have dropped to 7ish) and the cross-seeded wild-type was in Phosphate buffer at pH 7.0. In the E46K cross-seeding manuscript, it appears that pH 7.5 Tris was used for all fibrilizations (https://doi.org/10.1073/pnas.2012435118).  In any event, both results point to the fact that at pH 7.0-7.5 under low-seed conditions (0.5%) the Type 4 polymorph can propagate in a seed specific manner.

(3) In the Results section of "The buffer environment can dictate polymorph during seeded nucleation", the authors reference previous cell biological and biochemical assays to support the polymorph-specific seeding of MSA and PD patients under the same buffer conditions. This discussion is juxtaposed with recent research that compares the in vivo biological activities of hPFF, ampLB as well as LB, particularly in terms of seeding activity and pathology. Notably, this research suggests that ampLB, rather than hPFF, can accurately model the key aspects of Lewy Body Diseases (LBD) (refer to: https://doi.org/10.1038/s41467-023-42705-5). The critical issue here is the need to reconcile the phenomena observed in vitro with those in in-vivo or in-cell models. Given the low seed concentration reported in these studies, it is imperative for the authors to provide a more detailed explanation as to why the possible similar conformation could lead to divergent pathologies, including differences in cell-type preference and seeding capability.  

We thank the reviewer for bring this recent report to our attention. The findings that ampLB and hPFF have different PK digestion patterns and that only the former is able to model key aspects of Lewy Body disease are in support of the seed-specific nature of some types of alpha-synuclein aggregation.  We have added this to the discussion regarding the significant role that seed type and seed conditions likely play in polymorph selection.

(4) In the Method section of "Image processing", the authors describe the helical reconstruction procedure, without mentioning much detail about the 3D reconstruction and refinement process. For the benefit of reproducibility and to facilitate a deeper understanding among readers, the authors should enrich this part to include more comprehensive information, akin to the level of detail found in similar studies (refer to: https://doi.org/10.1038/nature23002).

As also suggested by reviewer #2, we have now added more comprehensive information on the 3D reconstruction and refinement process.

(5) The abbreviation of amino acids should be unified. In the Results section "On the structural heterogeneity of Type 1 polymorphs", the amino acids are denoted using three-letter abbreviation. Conversely, in the same section under "On the structural heterogeneity of Type 2 and 3 structures", amino acids are abbreviated using the one-letter format. For clarity and consistency, it is essential that a standardized format for amino acid abbreviations be adopted throughout the manuscript.

That makes perfect sense and had been corrected.

Reviewing Editor: 

After discussion among the reviewers, it was decided that point 2 in Reviewer #3's Public Review (about the experiments with different concentrations of seeds) would probably lie outside the scope of a reasonable revision for this work. 

We agree as stated above and will continue to work on this important point.

Revisions Round 2

Reviewer #2 (Public Review): 

I do worry that the FSC values of model-vs-map appear to be higher than expected from the corresponding FSCs between the half-maps (e.g. see Fig 13). The implication of this observation is that the atomic models may have been overfitted in the maps, which would have led to a deterioration of their geometry. A table with rmsd on bond lengths, angles, etc would probably show this. In addition, to check for overfitting, the atomic model for each data set could be refined in one of the half-maps, and then that same model could be used to calculate 2 FSC model-vs-map curves: one against the half-map it was refined in and one against the other half-map. Deviations between these two curves are an indication of overfitting. 

Thank you for the recommendations for model validation.  We have added the suggested statistics to Table 2 and performed the suggested model fitting to one of the half-maps and plotted 3 FSC model-vs-map curves: one for each half-map versus the model fit against only one half map and one for the model fit against the full map. We feel that the degree of overfitting is reasonable and does not  significantly impact the quality of the models. 

In addition, the sudden drop in the FSC curves in Figure 16 shows that something unexpected has happened to this refinement. Are the authors sure that only the procedures outlined in the Methods were used to create these curves? The unexpected nature of the FSC curve for this type (2A) raises doubts about the correctness of the reconstruction. 

We thank the reviewer for the attention to detail.  We should have caught this mistake. It turns out that in the last round of 3D refinement, the two half-maps become shifted with respect to each other in the z direction. We realigned the two maps using Chimera and then re-ran the postprocessing. The new maps have been deposited in EMD-50850. This mistake motivated us to inspect all of the maps and we found the same problem had occurred in the Type 3B maps.  This was not noticed by the reviewer because we accidentally plotted the FSC curves from postprocessing from one refinement round before the one deposited in the EMD. We performed the same half-map shifting procedure for the Type 3B data and performed a final round of real-space refinement to produce new maps and models that have been deposited as EMD-50888 and 9FYP (superseding the previous entries).

Reviewer #3 (Public Review): 

There are two minor points I recommend the authors to address: 

(1) In the response to Weakness 1, point (3), the authors state that "the Type 5 represented only 10-20% of the fibrils in the sample." However, this information is not labeled in the corresponding Figure 4. I suggest the authors verify and label all relevant percentages in the figures to prevent misunderstandings. 

We aim to be as transparent as possible and this information was included in the main text however we did not label the percentage of Type 5 fibrils in Figure 4 because that would make the other percentages ambiguous.  The percentages in Figure 4 represent the ratio of helical segments used for each type of refined structure in the dataset (always adding up to 100%), not the percent of all fibrils in the dataset.  That is, there are sometimes untwisted or unidentifiable fibrils in datasets and these were not accounted for in the listed percentages. We have added a sentence to the Figure 4 legend to explain to what the percentages refer.

(2) While the authors have detailed the helical reconstruction procedure in the Methods section, it is necessary to indicate the scale bar or box size in the figure legend of the 2D representative classes to ensure clarity and reproducibility. 

Thank you for reminding us to add the scale bars. This is now done for the 2D classes in Figures 11-17.

Recommendations for the authors: 

Reviewer #2 (Recommendations For The Authors): 

A critical look at the maps and models of the various structures at this stage may prevent the authors from entering suboptimal structures into the databases.  

We agree. Thank you for suggesting this.

Reviewer #3 (Recommendations For The Authors): 

The authors have responded adequately to these critiques in the revised version of the manuscript. There are two minor points. 

(1) The authors state that "the Type 5 represented only 10-20% of the fibrils in the sample." However, this information is not labeled in the corresponding Figure 4. I suggest the authors verify and label all relevant percentages in the figures to prevent misunderstandings. 

(2) While the authors have detailed the helical reconstruction procedure in the Methods section, it is necessary to indicate the scale bar or box size in the figure legend of the 2D representative classes to ensure clarity and reproducibility. 

Answered in public comments

eLife assessment

Using multiple public datasets, this study investigates associations between retrotransposon element expression and methylation with age and inflammation. The study is valuable because a systematic analysis of retrotransposon element expression during human aging has been lacking, but the provided data must be considered incomplete due to the sole reliance on microarray expression data for the core analyses.

Reviewer #1 (Public Review):

Tsai and Seymen et al. investigate associations between RTE expression and methylation and age and inflammation, using multiple public datasets. Compared to the previous round of review, the text of the manuscript has been polished and the phrasing of several findings has been made clearer and more precise. The authors also provided ample discussion to the prior reviewer comments in their rebuttal, including new analyses. All these changes are in the correct direction, however, I believe that part of the content of the rebuttal should be incorporated in the main text, for reasons that I will outline below.

Both reviewers found the reliance on microarray expression data to detract from the study. The authors argued that their choices are supported by existing publications which performed a similar quantification of TE expression using microarray data. It could still be argued that (as far as I can tell) Reichmann et al. used a substantially larger number of probes than this study, as a consequence of starting from different arrays, however, this is a minor point which the authors do not need to address. It is still undeniable that including the validation with RNA-seq data performed in the rebuttal would strengthen the manuscript. I especially believe that many readers would want to see this analysis be prominent in the manuscript, considering that both reviewers independently converged on the issue with microarray expression data. Personally, I would have included an RNA-seq dataset next to the microarray data in the main figures, however, I understand that this would require considerable restructuring and that placing RNA-seq data besides array data might be misleading. Instead, I would ask that the authors include their rebuttal figures R1 and R2 as supplementary figures.<br /> I would suggest introducing a new paragraph, between the section dedicated to expression data and the one dedicated to DNA methylation, mentioning the issues with microarray data (Some of which were mentioned by the reviewers and other which were mentioned by the authors in the discussion and introduction) to then introduce the validation with RNA-seq data.

Figure R3 is also a good addition and should be expanded to include the GTP and MESA study and possibly mentioned in the paragraph titled "RTE expression positively correlates with BAR gene signature scores except for SINEs."

"In this study, we did not compare MESA with GTP etc. We have analysed each dataset separately based on the available data for that dataset. Therefore, sacrificing one analysis because of the lack of information from the other does not make sense. We would do that if we were after comparing different datasets. Moreover, the datasets are not comparable because they were collected from different types of blood samples."

Indeed, the datasets are not compared directly, but the associations between age, BER and TE expression for each dataset are plotted and discussed right next to each other. It is therefore natural to wonder if the differences between datasets are due to differences in the type of blood sample or if they are a consequence of the different probe sets. Using a common set of probes would help answer that question.

Author response:

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

eLife assessment 

This study investigates associations between retrotransposon element expression and methylation with age and inflammation, using multiple public datasets. The study is valuable because a systematic analysis of retrotransposon element expression during human aging has been lacking. However, the data provided are incomplete due to the sole reliance on microarray expression data for the core analysis of the paper. 

Both reviewers found this study to be important. We have selected the microarray datasets of human blood adopted by a comprehensive study of ageing published in a Nature

Communications manuscript (DOI: doi: 10.1038/ncomms9570). We only included the datasets specifically collected for ageing studies. Therefore, the large RNA-seq cohorts for cancer, cardiovascular, and neurological diseases were not relevant to this study and cannot be included.   

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Tsai and Seymen et al. investigate associations between RTE expression and methylation and age and inflammation, using multiple public datasets. The concept of the study is in principle interesting, as a systematic analysis of RTE expression during human aging is lacking. 

We thank the reviewer for the positive comment. 

Unfortunately, the reliance on expression microarray data, used to perform the core analysis of the paper places much of the study on shaky ground. The findings of the study would not be sufficiently supported until the authors validate them with more suitable methods. 

In our discussion section in the manuscript, we have clarified that “we are aware of the limitations imposed by using microarray in this study, particularly the low number of intergenic probes in the expression microarray data. Our study can be enriched with the advent of large  RNA-seq cohorts for aging studies in the future.”  However, the application of microarray for RTE expression analysis was introduced previously (DOI: 10.1371/journal.pcbi.1002486) and applied in some highly cited and important publications before (DOI: 10.1038/ncomms1180, DOI: 10.1093/jnci/djr540). In fact, in a manuscript published by Reichmann et al.  (DOI: 10.1371/journal.pcbi.1002486) which was cited 76 times, the authors showed and experimentally verified that cryptic repetitive element probes present in Illumina and Affymetrix gene expression microarray platforms can accurately and sensitively monitor repetitive element expression data. Inspired by this methodological manuscript with reasonable acceptance by other researchers, we trusted that the RTE microarray probes could accurately quantify RTE expression at class and family levels.

Strengths: 

This is a very important biological problem. 

Weaknesses: 

RNA microarray probes are obviously biased to genes, and thus quantifying transposon analysis based on them seems dubious. Based on how arrays are designed there should at least be partial (perhaps outdated evidence) that the probe sites overlap a protein-coding or non-coding RNA. 

We disagree with the reviewer that quantifying transposon analysis based on microarray data is dubious. As previously shown by Reichmann et al., the quantification is reliable as long as the probes do not overlap with annotated genes and they are in the correct orientation to detect sense repetitive element transcripts. Reichman et al. identified 1,400 repetitive element probes in version 1.0, version 1.1 and version 2.0 of the Illumina Mouse WG-6 Beadchips by comparing the genomic locations of the probes with the Repeatmasked regions of the mouse genome. We applied the same criteria for Illumina Human HT-12 V3 (29431 probes) and V4 (33963) to identify the RTE-specific probes. 

The authors state they only used intergenic probes, but based on supplementary files, almost half of RTE probes are not intergenic but intronic (n=106 out of 264). 

All our identified RTE probes overlap with intergenic regions. However, due to their repetitive natures, some probes overlap with intronic regions, too. We have replaced "intergenic" with "non-coding" in our resubmission to show that they do not overlap with the exons of protein-coding genes. However, we do not rule out the possibility that some of our detected RTE probes might overlap non-coding RNAs. In fact, the border between coding and non-coding genomes has recently become very fuzzy with new annotations of the genome. RTE RNAs can be easily considered as non-coding RNAs if we challenge our traditional junk DNA view. 

This is further complicated by the fact that not all this small subset of probes is available in all analyzed datasets. For example, 232 probes were used for the MESA dataset but only 80 for the GTP dataset. Thus, RTE expression is quantified with a set of probes which is extremely likely to be highly affected by non-RTE transcripts and that is also different across the studied datasets. Differences in the subsets of probes could very well explain the large differences between datasets in multiple of the analyses performed by the authors, such as in Figure 2a, or 3a. It is nonetheless possible that the quantification of RTE expression performed by the authors is truly interpretable as RTE expression, but this must be validated with more data from RNA-seq. Above all, microarray data should not be the main type of data used in the type of analysis performed by the authors. 

In this study, we did not compare MESA with GTP etc. We have analysed each dataset separately based on the available data for that dataset. Therefore, sacrificing one analysis because of the lack of information from the other does not make sense. We would do that if we were after comparing different datasets. Moreover, the datasets are not comparable because they were collected from different types of blood samples. 

Reviewer #2 (Public Review): 

Summary: 

Yi-Ting Tsai and colleagues conducted a systematic analysis of the correlation between the expression of retrotransposable elements (RTEs) and aging, using publicly available transcriptional and methylome microarray datasets of blood cells from large human cohorts, as well as single-cell transcriptomics. Although DNA hypomethylation was associated with chronological age across all RTE biotypes, the authors did not find a correlation between the levels of RTE expression and chronological age. However, expression levels of LINEs and LTRs positively correlated with DNA demethylation, and inflammatory and senescence gene signatures, indicative of "biological age". Gene set variation analysis showed that the inflammatory response is enriched in the samples expressing high levels of LINEs and LTRs. In summary, the study demonstrates that RTE expression correlates with "biological" rather than "chronological" aging. 

Strengths: 

The question the authors address is both relevant and important to the fields of aging and transposon biology. 

We thank the reviewer for finding this study relevant and important.

Weaknesses: 

The choice of methodology does not fully support the primary claims. Although microarrays can detect certain intergenic transposon sequences, the authors themselves acknowledge in the Discussion section that this method's resolution is limited. More critical considerations, however, should be addressed when interpreting the results. The coverage of transposon sequences by microarrays is not only very limited (232 unique probes) but also predetermined. This implies that any potential age-related overexpression of RTEs located outside of the microarray-associated regions, or of polymorphic intact transposons, may go undetected. Therefore, the authors should be more careful while generalising their conclusions. 

This is a bioinformatics study, and we have already admitted and discussed the limitations in the discussion section of this manuscript. All technologies have their own limitations, and this should not stop us from shedding light on scientific facts because of inadequate information. In the manuscript, we have discussed that all large and proper ageing studies were performed using microarray technology. Peters et al. (DOI: doi: 10.1038/ncomms9570) adopted all these datasets in their transcriptional landscape of ageing manuscript, which was used in previous studies of ageing as well. Our study essentially applies the Reichmann et al. method to the peripheral blood-related data from the Peters et al. manuscript. Since hypomethylation due to ageing is a well-established and broad epigenetic reprogramming, it is unlikely that only a fraction of RTEs is affected by this phenomenon. Therefore, the subsampling of RTEs should not affect the result so much. Indeed, this is supported in our study by the inverse correlation between DNA methylation and RTE expression for LINE and SINE classes despite having limited numbers of probes for LINE and SINE expressions.    

Additionally, for some analyses, the authors pool signals from RTEs by class or family, despite the fact that these groups include subfamilies and members with very different properties and harmful potentials. For example, while sequences of older subfamilies might be passively expressed through readthrough transcription, intact members of younger groups could be autonomously reactivated and cause inflammation. The aggregation of signals by the largest group may obscure the potential reactivation of smaller subgroups. I recommend grouping by subfamily or, if not possible due to the low expression scores, by subgroup. For example, all HERV subfamilies are from the ERVL family. 

We agree with the reviewer that different subfamilies of RTEs play different roles through their activation. However, we will lose our statistical power if we study RTE subfamilies with a few probes. Global epigenetic alteration and derepression of RTEs by ageing have been observed to be genome-wide. While our systematic analysis across RTE classes and families cannot capture alterations in subfamilies due to statistical power, it is still relevant to the research question we are addressing.

Next, Illumina arrays might not accurately represent the true abundance of TEs due to nonspecific hybridization of genomic transposons. Standard RNA preparations always contain traces of abundant genomic SINEs unless DNA elimination is specifically thorough. The problem of such noise should be addressed. 

We have checked the RNA isolation step from MESA, GTP, and GARP manuscripts. The total RNA was isolated using the Qiagen mini kit following the manufacturer’s recommendations. The authors of these manuscripts did not mention whether they eliminated genomics DNA, but we assumed they were aware of the DNA contamination and eliminated it based on the manufacturer’s recommendations. We have looked up the literature about nonspecific hybridization of RTEs but could not find any evidence to support this observation. We would appreciate the reviewers providing more evidence about such RTE contaminations.   

Lastly, scRNAseq was conducted using 10x Genomics technology. However, quantifying transposons in 10x sequencing datasets presents major challenges due to sparse signals. 

Applying the scTE pipeline (https://www.nature.com/articles/s41467-021-21808-x), we have found that the statical power of quantifying RTE classes (LINE, SINE, and LTR) or  RTE families (L1, L2, All, ERVK, etc.) are as good as each individual gene. However, our proposed method cannot analyse RTE subfamilies, and we did not do that. 

Smart-seq single-cell technology is better suited to this particular purpose. 

We agree with the reviewer that Smart-seq provides higher yield than 10x, but there is no Smartseq data available for ageing study.  

Anyway, it would be more convincing if the authors demonstrated TE expression across different clusters of immune cells using standard scRNAseq UMAP plots instead of boxplots. 

Since the number of RTE reads per cell is low, showing the expression of RTEs per cell in UMAP may not be the best statistical approach to show the difference between the aged and young groups. This is why we chose to analyse with Pseudobulk and displayed differential expression using boxplot rather than UMAP for each immune cell type. 

I recommend validating the data by RNAseq, even on small cohorts. Given that the connection between RTE overexpression and inflammation has been previously established, the authors should consider better integrating their observations into the existing knowledge. 

Please see below. We have analysed RNA-seq data suggested by Reviewer 1 in the Recommendations for the Authors section.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

I can recommend two sizeable human PMBC RNA-seq datasets that the authors could use:

Marquez et al. 2020 (phs001934.v1.p1, controlled access) and Morandini et al. 2023 (GSE193141, public access). There are likely other suitable datasets that I am not aware of. I would also recommend using identical sets of probes to quantify RTE expression across studies. If certain datasets have too few probes and would thus limit the number of probes available across all studies it might be a good idea to exclude the dataset, especially if the analysis has been supplemented by the additional RNA-seq datasets. 

Until recently, there was no publicly-available, non-cancerous, large cohort of RNA-seq data for ageing studies. We tried to gain access to the two RNA-seq datasets suggested by reviewer 2: Marquez et al. 2020 (phs001934.v1.p1, controlled access) and Morandini et al. 2023 (GSE193141, public access). 

Unfortunately, Marquez et al. 2020 data is not accessible because the authors only provide the data for projects related to cardiovascular diseases. However, we did analyse Morandini et al. 2023 data, and we can confirm that no association was observed between any class and family of RTEs with chronological ageing (Author response image 1), which is the second strong piece of evidence supporting the statement in the manuscript. However, as expected, we found a positive correlation between RTE expression and IFN-I signature score (Author response image 2).

Author response image 1.

Linear analysis of RTE expression and chronological age.

Author response image 2.

Linear analysis of RTE expression and IFN gene signature expression.

The authors use "biological age" and inflammation as interchangeable concepts, including in the title. Please correct this wording. 

We have now added a new terminology to the manuscript called “biological age-related (BAR)”, which has been clearly addressed this distinction. We don’t think it is needed to change the title.  

The authors find correlations between RTE expression and age-associated gene signatures but not chronological age itself. This is puzzling because, as the wording suggests, the expression of these inflammatory pathways is age-associated. If RTE expression correlates with inflammation which itself correlates with age, one might expect RTE expression to also correlate with age. Do the authors see a correlation between various inflammatory gene signatures and chronological age, in the analyzed datasets? If yes, then how would you explain that discrepancy? Moreover, in this case, I would recommend using a linear model, rather than correlation, to separate the effects of chronological age and RTE expression on inflammation (Inflammation et al ~ Age + RTE expression), or equivalent designs.

As described above, we have now introduced the BAR terminology, which resolves this confusion. We did not find a correlation between RTE expression and chronological age. However, we did identify the correlation between BAR gene signatures and RTE expression.

To separate the effects of chronological age and RTE expression on BAR gene signature scores, we performed a generalized linear model (GLM) analysis using BAR gene signature scores as response variables and RTE expression and chronological age as predictors (BAR gene signature scores ~ RTE expression + chronological age). Significant association was observed between BAR gene signature scores and RTE expression in the GARP cohort (Author response image 3). However, when chronological age is considered as predictor, we did not identify a correlation between chronological age and BAR gene signatures, indicating that BAR events are not corelated with chronological age (Author response image 3).  

Author response image 3.

Generalized linear models (GLM) analysis (BAR gene signature scores ~ RTE expression + chronological age). For each RTE family, we separately performed GLM. Age (RTE family) indicates the chronological age when used in the design formula for that specific RTE family. 

Some of the gene sets used by the authors have considerable overlap with others and are also not particularly comprehensive. I can recommend this very comprehensive gene set: https://www.gsea-msigdb.org/gsea/msigdb/human/geneset/SAUL_SEN_MAYO.  

We did not choose to use large gene lists such as the suggested SEN_MAYO list, as we found Singscore struggles to generate reliable scores with sufficient variance when the number of genes increase to more than twenty. Although there is some overlap between inflammation-related genes and cellular senescence genes (e.g., IL6, IL1A, IL1B), it is important to note that each gene list focuses on different aspects of biological aging and should not be dismissed as redundant.

Minor comments: 

Overall, several sentences in the manuscript feel somewhat unnatural. I would recommend further proofreading. I will mention some examples:  

Thank you for your feedback. We have fixed all these issues in the new submission.  

• One line 34, "like the retroviruses" should be "like retroviruses. There are several other places in the text where "the" is not required. 

Fixed.

• On line 86, "to generate the RTE expression". "the" is again not necessary and I would replace "generate" with "quantify". 

Fixed.

• On line 86, "we mapped the probe locations to RepeatMasker". RepeatMasker is not a genome. Do you mean you mapped the probe location to a genome annotated by RepeatMasker? The same applies to line 99.  

Fixed. We changed the sentence to: “To quantify RTE expression, we mapped the microarray probe locations to RTE locations in RepeatMasker to extract the list of noncoding (intergenic or intronic) probes that cover the RTE regions.”

• Figure 1 contains a typo in the aims section: "evetns" instead of "events".  

Fixed.

• On line 495 "filtered out" seems to imply your removed intergenic probes. I assume you mean that you specifically selected intergenic probes. 

Fixed.

• Figure 1 nicely summarizes your datasets. Could you add a Figure 1b panel showing how you used RNA arrays to quantify RTE expression? This should include the number of probes for each RTE family, so I suggest merging this with Figure S1.  

We disagree with the reviewer to merge Figure 1 and Figure S1 because they are addressing two different concepts.  

Reviewer #2 (Recommendations For The Authors): 

In Figure 2c, it is unclear what colour scale has been used for age. 

Thank you for the comment. We have added a legend for age in this figure.

There are no figure legends for Supplementary Figures 1 to 5 and all figures after Supplementary Figure 8. 

A new version with legends has been submitted.

For different datasets used, the choice of "healthy" patients should be more clear and explicit.

Are asymptomatic patients with autoimmune inflammatory disorders considered as "healthy"? If not only healthy patients' blood is analysed (such as PBMS from primary osteoarthrosis), how inflammatory signatures enrichment discovered in this study may be associated not just with "biological age" but with the disease itself? 

In our analysis, we did not exclusively study "healthy" individuals, as none of our datasets were initially collected from strictly healthy populations. While the microarray datasets were not specifically collected from people with particular diseases, they were also not screened for asymptomatic conditions. To demonstrate the same pattern in healthier cohorts, we added scRNA-seq analysis of confirmed healthy individuals to our study. However, the focus of this study is not on healthy aging. Instead, it is on biological ageing that includes both healthy and non-healthy ageing.

We included the GARP (primary osteoarthritis) dataset as it is a cohort of age-related diseases (ARD). While we cannot definitively attribute inflammatory signatures enrichment to biological aging or disease, the observation of such enrichment in a cohort of ARD is worth considering. To make this clearer, we have replaced the term “healthy” with “non-cancerous” for microarray analysis throughout the paper.

Reviewer #1 (Public Review):

In this study, the authors introduced an essential role of AARS2 in maintaining cardiac function. They also investigated the underlying mechanism that through regulating alanine and PKM2 translation are regulated by AARS2. Accordingly, a therapeutic strategy for cardiomyopathy and MI was provided. Several points need to be addressed to make this article more comprehensive:

(1) Include apoptotic caspases in Figure 2B, and Figure 4 B and E as well.

(2) It would be better to show the change of apoptosis-related proteins upon the knocking down of AARS2 by small interfering RNA (siRNA).

(3) In Figure 5, the authors performed Mass Spectrometry to assess metabolites of homogenates. I was wondering if the change of other metabolites could be provided in the form of a heatmap.

(4) The amounts of lactate should be accessed using a lactate assay kit to validate the Mass Spectrometry results.

(5) How about the expression pattern of PKM2 before and after mouse MI. Furtherly, the correlation between AARS2 and PKM2?

(6) In Figure 5, how about the change of apoptosis-related proteins after administration of PKM2 activator TEPP-46?

eLife assessment

This valuable study demonstrates that AARS2 is crucial for protecting cardiomyocytes from ischemic stress by shifting energy metabolism towards glycolysis through PKM2, presenting a novel therapeutic target for myocardial infarction. The findings are supported by solid evidence, including cardiomyocyte-specific genetic modifications, functional assays, and ribosome profiling, which together robustly validate the AARS2-PKM2 signaling pathway's role in cardiac protection.

Reviewer #2 (Public Review):

Summary:

The authors aimed to elucidate the role of AARS2, an alanyl-tRNA synthase, in mouse hearts, specifically its impact on cardiac function, fibrosis, apoptosis, and metabolic pathways under conditions of myocardial infarction (MI). By investigating the effects of both deletion and overexpression of AARS2 in cardiomyocytes, the study aims to determine how AARS2 influences cardiac health and survival during ischemic stress.

The authors successfully achieved their aims by demonstrating the critical role of AARS2 in maintaining cardiomyocyte function under ischemic conditions. The evidence presented, including genetic manipulation results, functional assays, and mechanistic studies, robustly supports the conclusion that AARS2 facilitates cardiomyocyte survival through PKM2-mediated metabolic reprogramming. The study convincingly links AARS2 overexpression to improved cardiac outcomes post-MI, validating the proposed protective AARS2-PKM2 signaling pathway.

This work may have a significant impact on the field of cardiac biology and ischemia research. By identifying AARS2 as a key player in cardiomyocyte survival and metabolic regulation, the study opens new avenues for therapeutic interventions targeting this pathway. The methods used, particularly the cardiomyocyte-specific genetic models and ribosome profiling, are valuable tools that can be employed by other researchers to investigate similar questions in cardiac physiology and pathology.

Understanding the metabolic adaptations in cardiomyocytes during ischemia is crucial for developing effective treatments for MI. This study highlights the importance of metabolic flexibility and the role of specific enzymes like AARS2 in facilitating such adaptations. The identification of the AARS2-PKM2 axis adds a new layer to our understanding of cardiac metabolism, suggesting that enhancing glycolysis can be a viable strategy to protect the heart from ischemic damage.

Strengths:

(1) Comprehensive Genetic Models: The use of cardiomyocyte-specific AARS2 knockout and overexpression mouse models allowed for precise assessment of AARS2's role in cardiac cells.

(2) Functional Assays: Detailed phenotypic analyses, including measurements of cardiac function, fibrosis, and apoptosis, provided evidence for the physiological impact of AARS2 manipulation.

(3) Mechanistic Insights: This study used ribosome profiling (Ribo-Seq) to uncover changes in protein translation, specifically highlighting the role of PKM2 in metabolic reprogramming.

(4) Therapeutic Relevance: The use of the PKM2 activator TEPP-46 to reverse the effects of AARS2 deficiency presents a potential therapeutic avenue, underscoring the practical implications of the findings.

Weaknesses:

(1) Species Limitation: The study is limited to mouse and rat models, and while these are highly informative, further validation in human cells or tissues would strengthen the translational relevance.

(2) Temporal Dynamics: The study does not extensively address the temporal dynamics of AARS2 expression and PKM2 activity during the progression of MI and recovery, which could offer deeper insights into the timing and regulation of these processes.

Reviewer #3 (Public Review):

In the present study, the author revealed that cardiomyocyte-specific deletion of mouse AARS2 exhibited evident cardiomyopathy with impaired cardiac function, notable cardiac fibrosis, and cardiomyocyte apoptosis. Cardiomyocyte-specific AARS2 overexpression in mice improved cardiac function and reduced cardiac fibrosis after myocardial infarction (MI), without affecting cardiomyocyte proliferation and coronary angiogenesis. Mechanistically, AARS2 overexpression suppressed cardiomyocyte apoptosis and mitochondrial reactive oxide species production, and changed cellular metabolism from oxidative phosphorylation toward glycolysis in cardiomyocytes, thus leading to cardiomyocyte survival from ischemia and hypoxia stress. Ribo-Seq revealed that AARS2 overexpression increased pyruvate kinase M2 (PKM2) protein translation and the ratio of PKM2 dimers to tetramers that promote glycolysis. Additionally, PKM2 activator TEPP-46 reversed cardiomyocyte apoptosis and cardiac fibrosis caused by AARS2 deficiency. Thus, this study demonstrates that AARS2 plays an essential role in protecting cardiomyocytes from ischemic pressure via fine-tuning PKM2-mediated energy metabolism, and presents a novel cardiac protective AARS2-PKM2 signaling during the pathogenesis of MI. This study provides some new knowledge in the field, and there are still some questions that need to be addressed in order to better support the authors' views.

(1) WGA staining showed obvious cardiomyocyte hypertrophy in the AARS2 cKO heart. Whether AARS affects cardiac hypertrophy needs to be further tested.

(2) The authors observed that AARS2 can improve myocardial infarction, and whether AARS2 has an effect on other heart diseases.

(3) Studies have shown that hypoxia conditions can lead to mitochondrial dysfunction, including abnormal division and fusion. AARS2 also affects mitochondrial division and fusion and interacts with mitochondrial proteins, including FIS and DRP1, the authors are suggested to verify.

(4) The authors only examined the role of AARS2 in cardiomyocytes, and fibroblasts are also an important cell type in the heart. Authors should examine the expression and function of AARS2 in fibroblasts.

(5) Overexpression of AARS2 can inhibit the production of mtROS, and has a protective effect on myocardial ischemia and H/ R-induced injury, and the occurrence of iron death is also closely related to ROS, whether AARS protects myocardial by regulating the occurrence of iron death?

(6) Please revise the English grammar and writing style of the manuscript, spelling and grammatical errors should be excluded.

(7) Recent studies have shown that a decrease in oxygen levels leads to an increase in AARS2, and lactic acid rises rapidly without being oxidized. Both of these factors inhibit oxidative phosphorylation and muscle ATP production by increasing mitochondrial lactate acylation, thereby inhibiting exercise capacity and preventing the accumulation of reactive oxygen species ROS. The key role of protein lactate acylation modification in regulating oxidative phosphorylation of mitochondria, and the importance of metabolites such as lactate regulating cell function through feedback mechanisms, i.e. cells adapt to low oxygen through metabolic regulation to reduce ROS production and oxidative damage, and therefore whether AARS2 in the heart also acts in this way.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Little is known about the local circuit mechanisms in the preoptic area (POA) that regulate body temperature. This carefully executed study investigates the role of GABAergic interneurons in the POA that express neurotensin (NTS). The principal finding is that GABA-release from these cells inhibits neighboring neurons, including warm-activated PACAP neurons, thereby promoting hyperthermia, whereas NTS released from these cells has the opposite effect, causing a delayed activation and hypothermia. This is shown through an elegant series of experiments that include slice recordings alongside matched in vivo functional manipulations. The roles of the two neurotransmitters are distinguished using a cell-type-specific knockout of Vgat as well as pharmacology to block GABA and NTS receptors. Overall, this is an excellent study that is noteworthy for revealing local circuit mechanisms in the POA that control body temperature and also for highlighting how amino acid neurotransmitters and neuropeptides released from the same cell can have opposing physiologic effects. I have only minor suggestions for revision.

Reviewer #2 (Public Review):

Summary:

The study has demonstrated how two neurotransmitters and neuromodulators from the same neurons can be regulated and utilized in thermoregulation.

The study utilized electrophysiological methods to examine the characteristics and thermoregulation of Neurotensin (Nts)-expressing neurons in the medial preoptic area (MPO). It was discovered that GABA and Nts may be co-released by neurons in MPO when communicating with their target neurons.

Strengths:

The study has leveraged optogenetic, chemogenetic, knockout, and pharmacological inhibitors to investigate the release process of Nts and GABA in controlling body temperature.

The findings are relevant to those interested in the various functions of specific neuron populations and their distinct regulatory mechanisms on neurotransmitter/neuromodulator activities

Weaknesses:

Key points for consideration include:

(1) The co-release of GABA and Nts is primarily inferred rather than directly proven. Providing more direct evidence for the release of GABA and the co-release of GABA and Nts would strengthen the argument. Further in vitro analysis could strengthen the conclusion regarding this co-releasing process.

Measurement of Nts concentrations in various brain regions during thermoregulatory responses is part of a future study.

(2) The differences between optogenetic and chemogenetic methods were not thoroughly investigated. A comparison of in vitro results and direct observation of release patterns could clarify the mechanisms of GABA release alone or in conjunction with Nts under different stimulation techniques.

A comparison of chemogenetic and optogenetic stimulation methods is not within the scope of this study.

(3) Neuronal transcripts were mainly identified through PCR, and alternative methods like single-cell sequencing could be explored.

Single cell transcriptomics of preoptic neurotensinergic neurons will be part of a different study.

(4) In Figure 6, the impact of GABA released from Nts neurons in MPO on CBT regulation appears to vary with ambient temperatures, requiring a more detailed explanation for better comprehension.

The different possible roles of GABA in different thermoregulatory circumstances is discussed on lines 555-581.

(5) The model should emphasize the key findings of the study.

The model is presented in Fig 8.

Reviewer #3 (Public Review):

Summary:

Understanding the central neural circuits regulating body temperature is critical for improving health outcomes in many disease conditions and in combating heat stress in an ever-warming environment. The authors present important and detailed new data that characterizes a specific population of POA neurons with a relationship to thermoregulation. The new insights provided in this manuscript are exactly what is needed to assemble a neural network model of the central thermoregulatory circuitry that will contribute significantly to our understanding of regulating the critical homeostatic variable of body temperature. These experiments were conducted with the expertise of an investigator with career-long experience in intracellular recordings from POA neurons. They were interpreted conservatively in the appropriate context of current literature.

The Introduction begins with "Homeotherms, including mammals, maintain core body temperature (CBT) within a narrow range", but this ignores the frequent hypothermic episodes of torpor that mice undergo triggered by cold exposure. Although the author does mention torpor briefly in the Discussion, since these experiments were carried out exclusively in mice, greater consideration (albeit speculative) of the potential for a role of MPO Nts neurons in torpor initiation or recovery is warranted. This is especially the case since some 'torpor neurons' have been characterized as PACAP-expressing and a population of PACAP neurons represent the target of MPO Nts neurons.

Additional discussion of a possible role of neurotensinergic neurons in the initiation or recovery from torpor is included (lines 593-597).

eLife assessment

This study provides compelling data that defines the structure of the S. cerevisiae APC/C. The structure reveals overall conservation of its mechanism of action compared to the human APC/C but some important differences that indicate that activation by co-activator binding and phosphorylation are not identical to the human APC/C. Thus this study will be of considerable value to the field, although the conclusions regarding the effect of phosphorylation would be strengthened by quantification of the phosphopeptides. Recent work on the role of APC7 in APC/C activity in neurones should also be discussed with respect to the mode of action of the APC/C in human versus budding yeast cells.

Reviewer #1 (Public Review):

Summary:

This work focuses on the structure and regulation of the Anaphase-Promoting Complex/Cyclosome (APC/C), a large multi-subunit ubiquitin ligase that controls the onset of chromosome segregation in mitosis. Previous high-resolution structural studies have uncovered numerous structural features and regulatory mechanisms of the human APC/C, but it has remained unclear if these mechanisms are conserved in other model eukaryotes. To address this gap in our understanding, the authors employed cryo-electron microscopy to generate structural models of APC/C from the budding yeast S. cerevisiae, a key model organism in cell cycle analysis. In their comparison of the human and yeast complexes, the authors uncover many conserved structural features that are documented here in detail, revealing widespread similarities in the fundamental structural features of the enzyme. Interestingly, the authors also find evidence that two of the key mechanisms of human APC/C regulation are not conserved in the yeast enzyme. Specifically:

(1) The ubiquitin ligase activity of the APC/C depends on its association with a co-activator subunit such as CDH1 or CDC20, which serves both as a substrate-binding adaptor and as an activator of interactions with the E2 co-enzyme. Previous studies of the human APC/C revealed that co-activator binding induces a conformational change that enables E2 binding. In contrast, the current work shows that this E2-binding conformation already exists in the absence of a co-activator in the yeast enzyme, suggesting that the enhancement of E2 binding in yeast depends on other, as yet undiscovered, mechanisms.

(2) APC/C phosphorylation on multiple subunits is known to enhance APC/C activation by the CDC20 co-activator in mitosis. Previous studies showed that phosphorylation acts by promoting the displacement of an autoinhibitory loop that occupies part of the CDC20-binding site. In the yeast enzyme, however, there is no autoinhibitory loop in the CDC20-binding site, and there is no apparent effect of APC/C phosphorylation on co-activator binding sites. Thus, phosphorylation activates the yeast CDC20-APC/C by unknown mechanisms.

Strengths:

The strength of this paper is that it provides a comprehensive analysis of yeast APC/C structure and how it compares to previously determined human structures. The article systematically unwraps the key features of the structure in a subunit-by-subunit fashion, carefully revealing the key features that are the same or different in the two species. These descriptions are based on a thorough overview of past work in the field; indeed, this article serves as a concise review of the key features, conserved or otherwise, of APC/C structure and regulation.

Weaknesses:

No significant weaknesses were identified.

Reviewer #2 (Public Review):

Summary:

This paper from the Barford lab describes medium/high-resolution cryo-EM structures of three versions of the S. cerevisiae anaphase-promoting complex/cyclosome (APC/C):

(1) the recombinant apo complex purified from insect cells,

(2) the apo complex phosphorylated in vitro by cyclin-dependent kinase, and

(3) an active APC/C-Cdh1-substrate ternary complex.

The focus of the paper is on comparing similarities and differences between S. cerevisiae and human APC/C structures, mechanisms of activation by coactivator, and regulation by phosphorylation. The authors find that the overall structures of S. cerevisiae and human APC/C are remarkably similar, including the binding sites and orientation for the substrate-recruiting coactivator, Cdh1. In addition, the mechanism of Cdh1 inhibition by phosphorylation appears conserved across kingdoms. However, key differences were also observed that reveal divergence in APC/C mechanisms that are important for researchers in this field to know. Specifically, the mechanism of APC/C-Cdc20 activation by mitotic phosphorylation appears to be different, due to the absence of the key Apc1 autoinhibition loop in the S. cerevisiae complex. In addition, the conformational activation of human APC/C by coactivator binding was not observed in the S. cerevisiae complex, implying that stimulation of E2 binding must occur via a different mechanism in this species.

Strengths:

Consistent with the numerous prior cryo-EM structures of human APC/C from the Barford lab, the technical quality of the structure models is a major strength of this work. In addition, the detailed comparison of similarities and differences between the two species will be a very valuable resource for the scientific community. The manuscript is written very well and allows readers lacking expertise in cryo-EM to understand the important aspects of the conservation of APC/C structure and mechanism across kingdoms.

Weaknesses:

The lack of experimentation in this work to test some of the putative differences in APC/C mechanism (e.g. stimulation of E2 binding by coactivator and stimulation of activity by mitotic phosphorylation) could be considered a weakness. Nonetheless, the authors do a nice job explaining how the structure interpretations imply these differences likely exist, and this work sets the stage nicely for future studies to understand these differences at a mechanistic level. There is enough value in having the S. cerevisiae structure models and the comparison to the human structures, without any additional experimentation.

The validation of APC/C phosphorylation in the unphosphorylated and hyperphosphorylated states is not very robust. Given the lack of significant effects of phosphorylation on APC/C structure observed here (compared to the human complex), this becomes important. A list of phosphorylation sites identified by mass spec before and after in vitro phosphorylation is provided but lacks quantitative information. This list indicates that a significant number of phosphorylation sites are detected in the purified APC/C prior to reaction with purified kinases. Many more sites are detected after in vitro kinase reaction, but it isn't clear how extensively any of the sites are modified. There is reason for caution then, in accepting the conclusions that structures of unphosphorylated and hyperphosphorylated APC/C from S. cerevisiae are nearly identical.

Reviewer #3 (Public Review):

Vazquez-Fernandez et al. present a comprehensive and detailed analysis of the S. cerevisiae APC/C complex, providing new insights into its structure and function. The authors determined the medium-resolution structures of three recombinant S. cerevisiae APC/C complexes, including unphosphorylated apo-APC/C (4.9 Å), the ternary APC/CCDH1-substrate complex (APC/CCDH1:Hsl1 , 4.0 Å), and phosphorylated apo-APC/C (4.4 Å). Prior structures of human, E. cuniculi, S. cerevisiae, and S. pombe APC/C subunits, as well as AlphaFold2 predictions were used to guide model building. Although the determined structures are not sufficient to fully explain the molecular mechanism of APC/C activation and regulation in S. cerevisiae, they provide valuable insights into the similarities and differences with the human complex, shedding light on the conserved and divergent features of APC/C function.

The manuscript synthesizes the structural analysis of the APC/C complex in S. cerevisiae, with literature into a cohesive and clear picture of the complex's structure and function. It is well-written and clear, making the complex biology of the APC/C complex accessible to a wide range of readers. The complex forms a triangular shape, with a central cavity surrounded by two modules: the TPR lobe and the platform module. The TPR lobe consists of three TPR proteins (APC3, APC6, and APC8), which stack on top of each other to form a quasi-symmetric structure. The platform module is composed of the large APC1 subunit, together with APC4 and APC5. The authors also analyzed the structure of several smaller subunits that are involved in regulating the activity of the APC/C complex and showed their structural similarities to and discrepancies from their human counterparts. These subunits, including CDC26/APC12, SWM1/APC13, APC9, and MND2/APC15, form extended, irregular structures that simultaneously contact multiple large globular APC/C subunits.

While the authors report the similarity between the overall structure of S. cerevisiae and human APC/C complexes, they also found two unexpected differences. First, in the S. cerevisiae apo-complex, the E2 binding site on APC11RING is accessible, whereas, in humans, it requires CDH1 binding. Second, a structural element similar to the human APC1 auto-inhibitory segment is missing in S. cerevisiae. In humans, the phosphorylation-dependent displacement of this segment allows CDC20 binding to APC/C. In S. cerevisiae, the binding requires phosphorylation however the structures reported here are suggestive that this could involve a different (presently unknown) mechanism. These structural insights highlight the importance of understanding the species-specific features of APC/C function.

Strengths:

The manuscript does a great job of revealing new structures.

Opportunity for increasing impact: It would have been nice if some functional differences were demonstrated, for example regarding the mechanism of CDC20 binding, and the comparison between apo-APC/C and ternary APC/CCDH1:Hsl1 does not explain the molecular activation mechanism of S. cerevisiae APC/C. Nonetheless, the authors nicely integrate their data with well-established literature on the similarities and differences between yeast and human systems.

Weaknesses:

The authors should cite and discuss Cole Ferguson et al., Mol Cell 2022. This study describes the loss of APC7 in human disease and provides a detailed structural and biochemical examination of the effects of APC7 loss on human APC/C. Given that much of our understanding of APC7 comes from this work, it should be highlighted in the introduction and discussed in depth in light of the new work on S. cerevisiae APC/C.

eLife assessment

This study assessed the virulence and immune responses of different M. tuberculosis lineages using a 3D in vitro granuloma model. The useful findings support the functional impact of M. tuberculosis natural diversity on host-pathogen interactions but are incomplete and only partially support the claims. The study will interest researchers working on mycobacteria and understanding how genetic diversity influences virulence and immunity outcomes.

Reviewer #1 (Public Review):

Summary:

This study further develops the potential of in vitro granulomas to study host-pathogen interactions in tuberculosis. It uses a human-based cellular model and a collection of M. tuberculosis isolates representative of the pathogen's diversity. It provides important methodologic information and some findings that help in defining protective responses in TB.

Strengths:

A strength of the study is the multitude of parameters addressed across different M. tuberculosis strains and donors. The inclusion of several strains of the same lineage shows that intra-lineage diversity is also relevant, illustrating how complex it is to model the immune response to M. tuberculosis.

Weaknesses:

A weakness of the study is that although several interesting findings are reported and a hypothesis proposed, the work is mainly descriptive and correlative. Some functional data based on the current observations would strengthen the findings.

Reviewer #2 (Public Review):

Summary:

This manuscript reports a comparison of microbial traits and host response traits in a laboratory model of infected granuloma using Mtb strains from different lineages. The authors report increased bacillary growth and granuloma formation, inversely associated with T cell activation that is characterized by CXCL9, granzyme B, and TNF expression. They therefore infer that these T cell responses are likely to be host-protective and that the greater virulence of modern Mtb lineages may be driven by their ability to avoid triggering these responses.

Strengths:

The comparison of multiple Mtb lineages in a granuloma model that enables evaluation of the potential role of multiple host cells in Mtb control offers a valuable experimental approach to studying the biological mechanisms that underpin differential virulence of Mtb lineages that have been previously reported in clinical and epidemiological studies.

Weaknesses:

The study is rather limited to descriptive observations and lacks experiments to test causal relationships between host and pathogen traits. Some of the presentation of the data is difficult to interpret, and some conclusions are not adequately supported by the data.

Reviewer #3 (Public Review):

Summary:

In "CXCL9, granzyme B, and TNF-α orchestrate protective in vitro granulomatous responses across Mycobacterium tuberculosis complex lineages", Arbués and colleagues describe the impact of mycobacterial genetic diversity on host-infection phenotypes. The authors evaluate Mtb infection and contextualize host responses, bacterial growth, and metabolic transitioning in vitro using their previously established model of blood-derived, primary human cells cultured on a collogen/fibronectin matrix. They seek to demonstrate the effectiveness of the model in determining mycobacterial strain-specific granuloma-dependent host-pathogen interactions.

Strengths and weaknesses:

Understanding the way mycobacterial genetic diversity impacts granuloma biology in tuberculosis is an important goal. One of this work's strengths is the use of primary human cells and two constituents of the pulmonary extracellular matrix to model Mtb infection. The authors and others have previously shown that Mtb-infected PBMC aggregates share important characteristics with early pulmonary TB granulomas (Arbues et al., Bio Protoc, 2020, PMID: 3659472; Guirado et al., mBio, 2015, PMID: 25691598; Kapoor et al., PloS One, 2013, PMID: 23308269). The use of multiple genetically distinct strains of Mtb defines this work and further bolsters its potential impact. However, the study is not comprehensive as lineages 6 and 7 are not tested. Experiments are primarily descriptive, and the methodologies are conventional. Correlative relationships are the manuscript's focus and functional validation is not conducted. Convoluted data presentation hampers the readers' ability to effectively evaluate many of the findings for significance. The effect sizes are generally small and most quantitative data are unitless. A further weakness of the study is a lack of any in vivo modeling.

Achievement of aims, and support for conclusions:

The main aim of this work is to extend an in vitro granuloma model to the study of a large collection of well-characterized, genetically diverse representatives of the mycobacterium tuberculosis complex (MTBC). I believe that they accomplish that aim. The work does investigate MTBC infection of aggregated PBMCs using three strains each of Mtb lineages 1-5 and H37Rv, which is not a trivial undertaking. The experimental aims are to show that MTBC genetic diversity impacts the growth and dormancy of granuloma-bound bacteria and, the host responses of granulomatous aggregation as well as macrophage apoptosis, lymphocyte activation, and soluble mediator release within granulomas. A lack of basic descriptive statistics for raw data makes it difficult to determine if benchmarks for most of the experimental aims have been reached. Although the methodologies employed should have been able to test most of these aims. The title's conclusion that CXCL9, granzyme B, and TNF orchestrate a protective granulomatous response is not tested and is not supported by the findings. Those molecules are not a focus of the work, their effects are not investigated effectively and their relationship to the granulomatous response is not determined. The authors' conclusions regarding their results are a mixed bag. Their conclusion that lineage impacts growth within granulomas is likely true and the data as presented reflect such a relationship. However, even without the basic descriptive statistics needed to evaluate the data supporting that claim, the methods employed for bacterial collection call into question whether all Mtb plated for CFU assay resided within granulomatous aggregates. Their conclusions regarding lineage's impact on dormancy are not supported, as their findings demonstrate that assays for dormancy identify replicating bacteria as being dormant. Their conclusion that strain diversity results in a spectrum of granulomatous responses in their model system is strongly supported by the results. Their conclusion that strain diversity impacts macrophage apoptosis is supported by the data but a relationship of apoptosis to the granulomatous response is not effectively evaluated. Their conclusion that lymphocyte activation is associated with reduced mycobacterial growth as an aspect of granulomas is well supported in the literature and a negative correlation between T cell activation and growth is supported by their results.

Impact on the field:

The authors contribute some valuable insights, particularly in Figure 3 and supplementary Figures 1 and 2, where data is more accessible to critique. Their identification of donor-dependent aggregation phenotypes by mycobacterial strain has the potential to enable future reverse-genetic screens for human and Mtb loci that contribute to granulomatous inflammation. Their model is a higher echelon relative to others in the field, but I don't believe that it possesses all of the necessary tissue and cellular components to effectively replicate the formation of granulomas in nature. The bulk of the data in its current form is not of high value to the community, but I think it has the potential to contribute additional novel insights if panels that display descriptive statistics are added to the figures.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Ever-improving techniques allow the detailed capture of brain morphology and function to the point where individual brain anatomy becomes an important factor. This study investigated detailed sulcal morphology in the parieto-occipital junction. Using cutting-edge methods, it provides important insights into local anatomy, individual variability, and local brain function. The presented work advances the field and will stimulate future research into this important area.

Strengths:

Detailed, very thorough methodology. Multiple raters mapped detailed sulci in a large cohort. The identified sulcal features and their functional and behavioural relevance are then studied using various complementary methods. The results provide compelling evidence for the importance of the described sulcal features and their proposed relationship to cortical brain function.

We thank the Reviewer for highlighting the strengths of our methods and findings.

Weaknesses:

A detailed description/depiction of the various sulcal patterns is missing.

We agree that adding these details for the newly described sulci is necessary and have now done so. These details are included in the Results (Page 6):

“Beyond characterizing the incidence of sulci, it is also common in the neuroanatomical literature to qualitatively characterize sulci on the basis of fractionation and intersection with surrounding sulci (termed “sulcal types”; for examples in other cortical expanses, see Chiavaras & Petrides, 2000; Drudik et al., 2023; Miller et al., 2021; Paus et al., 1996; Weiner et al., 2014; Willbrand, Parker, et al., 2022). All four sulci most commonly did not intersect with other sulci (see Supplementary Tables 1-4 for a summary of the sulcal types of the slocs and pAngs dorsal and ventral components). The sulcal types were also highly comparable between hemispheres (rs > .99 , ps < .001).”

And in four new Supplementary Tables.

A possible relationship between sulcal morphology and individual demographics might provide more insight into anatomical variability.

We have conducted additional analyses to relate sulcal incidence to demographic features (age and gender). These results are included on Pages 5-6:

“Given that sulcal incidence and patterning is also sometimes related to demographic features (Cachia et al., 2021; Leonard et al., 2009; Wei et al., 2017), subsequent GLMs relating the incidence and patterning of the three more variable sulci (slocs-d, pAngs-v, and pAngs-d) to demographic features (age and gender) revealed no associations for any sulcus (ps > .05).”

The unique dataset offers an opportunity to provide insights into laterality effects that should be explored.

We included hemisphere as a factor in all models for this exact reason. Throughout the paper, we have edited the text to ensure that these laterality effects are more apparent to readers.

Further, we have a Supplementary Results section on hemispheric effects regarding the slocs-v, cSTS3, and lTOS:

“Hemispheric asymmetries in morphological, architectural, and functional features with regards to the slocs-v, cSTS3, and lTOS comparison

We observed a sulcus x metric x hemisphere interaction on the morphological and architectural features of the slocs-v (F(4.20, 289.81) = 4.16, η2 = 0.01, p = .002; the cSTS3 is discussed in the next section). Post hoc tests showed that this interaction was driven by  the slocs-v being cortically thinner in the left than the right hemisphere (p < .001; Fig. 2a).

There was also a sulcus x network x hemisphere interaction on the functional connectivity profiles (using functional connectivity parcellations from (Kong et al., 2019)) of the slocs-v and lTOS (F(32, 2144) = 3.99, η2 = 0.06, p < .001; the cSTS3 is discussed in the next section). Post hoc tests showed that this interaction was driven by three effects: (i) the slocs-v overlapped more with the Default C subnetwork in the left than the right hemisphere (p = .013), (ii) the lTOS overlapped more with Visual A subnetwork in the right than the left hemisphere (p = .002), and (iii) the lTOS overlapped more with the Visual B subnetwork in the left than the right hemisphere (p = .002; Fig. 2b).”

As well as the other STS rami on morphology:

“It is also worth noting that there was a sulcus x metric x hemisphere interaction (F(4, 284.12) = 6.60, η2 = 0.08, p < .001). Post hoc tests showed that: (i) the cSTS3 was smaller (p < .001) and thinner (p = .025) in the left than the right hemisphere (Supplementary Fig. 8a), (ii) the cSTS2 was shallower (p = .004) and thicker (p < .001) in the right than left hemisphere (Supplementary Fig. 8a), and (iii) the cSTS1 was shallower (p < .001), smaller (p = .002), thinner (p = .001), and less myelinated (p < .001) in the left than the right hemisphere (Supplementary Fig. 8a).”

And functional connectivity of the STS rami:

“There was also a sulcus x network x hemisphere interaction (F(32, 2208) = 12.26, η2 = 0.15, p < .001). Post hoc tests showed differences for each cSTS component. Here, the cSTS1 overlapped more with the Auditory network (p < .001), less with the Control B subnetwork (p < .001), more with the Control C subnetwork (p < .001), less with the Default B subnetwork (p < .001), more with the Default C subnetwork (p < .001), more with the Ventral Attention B subnetwork (p < .001), and more with the Visual A subnetwork (p = .024) in the right than in the left hemisphere (Supplementary Fig. 8b). In addition, the cSTS2 overlapped more with the Control B subnetwork (p < .001), more with the Control C subnetwork (p < .001), less with the Default B subnetwork (p < .001), and less with the Temporal-Parietal network (p = .011) in the right than in the left hemisphere (Supplementary Fig. 8b). Finally, the cSTS3 overlapped more with the Control B subnetwork (p = .002), less with the Default B subnetwork (p = .014), more with the Default C subnetwork (p = .022), less with the Ventral Attention B subnetwork (p = .029) in the right than in the left hemisphere (Supplementary Fig. 8b).”

Reviewer #2 (Public Review):

Summary: After manually labeling 144 human adult hemispheres in the lateral parieto-occipital junction (LPOJ), the authors 1) propose a nomenclature for 4 previously unnamed highly variable sulci located between the temporal and parietal or occipital lobes, 2) focus on one of these newly named sulci, namely the ventral supralateral occipital sulcus (slocs-v) and compare it to neighboring sulci to demonstrate its specificity (in terms of depth, surface area, gray matter thickness, myelination, and connectivity), 3) relate the morphology of a subgroup of sulci from the region including the slocs-v to the performance in a spatial orientation task, demonstrating behavioral and morphological specificity. In addition to these results, the authors propose an extended reflection on the relationship between these newly named landmarks and previous anatomical studies, a reflection about the slocs-v related to functional and cytoarchitectonic parcellations as well as anatomic connectivity and an insight about potential anatomical mechanisms relating sulcation and behavior.

Strengths:

- To my knowledge, this is the first study addressing the variable tertiary sulci located between the superior temporal sulcus (STS) and intraparietal sulcus (IPS).

- This is a very comprehensive study addressing altogether anatomical, architectural, functional and cognitive aspects.

- The definition of highly variable yet highly reproducible sulci such as the slocs-v feeds the community with new anatomo-functional landmarks (which is emphasized by the provision of a probability map in supp. mat., which in my opinion should be proposed in the main body).

- The comparison of different features between the slocs-v and similar sulci is useful to demonstrate their difference.

- The detailed comparison of the present study with state of the art contextualizes and strengthens the novel findings.

- The functional study complements the anatomical description and points towards cognitive specificity related to a subset of sulci from the LPOJ

- The discussion offers a proposition of theoretical interpretation of the findings

- The data and code are mostly available online (raw data made available upon request).

We thank the Reviewer for highlighting the strengths of our methods, analyses, and applications of our findings.

Weaknesses:

- While three independent raters labeled all hemispheres, one single expert finalized the decision. Because no information is reported on the inter-rater variability, this somehow equates to a single expert labeling the whole cohort, which could result in biased labellings and therefore affect the reproducibility of the new labels.

Our group does not use an approach amenable to calculating inter-rater agreements to expedite the process of defining thousands of sulci at the individual level in multiple regions. Our method consists of a two-tiered procedure. Here, authors YT and TG defined sulci which were then checked by a trained expert (EHW). These were then checked again by senior author  (KSW) . We emphasize that this process has produced reproducible anatomical results in other regions such as posteromedial cortex (Willbrand et al., 2023 Science Advances; Willbrand et al., 2023 Communications Biology; Maboudian et al., 2024 The Journal of Neuroscience), ventral temporal cortex (Weiner et al., 2014 NeuroImage; Miller et al., 2020 Scientific Reports; Parker et al., 2023 Brain Structure and Function), and lateral prefrontal cortex (Miller et al., 2021 The Journal of Neuroscience; Voorhies et al., 2021 Nature Communications; Yao et al., 2022 Cerebral Cortex; Willbrand et al., 2022 Brain Structure and Function; Willbrand et al., 2023 The Journal of Neuroscience) across age groups, species, and clinical populations. Further, in the Supplemental Materials we provide post mortem images showing that these sulci exist outside of cortical reconstructions, supporting this updated sulcal schematic of the lateral parieto-occipital junction. For the present study, by the time the final tier of our method was reached, we emphasize that a very small percentage (~2%) of sulcal definitions were actually modified. We will include an exact percentage in future publications in LPC/LOPJ.

- 3 out of the 4 newly labeled sulci are only described in the very first part and never reused. This should be emphasized as it is far from obvious at first glance of the article.

We have edited the Abstract (shown below, on Page 1) and paper throughout to emphasize the emphasis on the slocs-v over the other three sulci.

“After defining thousands of sulci in a young adult cohort, we revised the previous LPC/LPOJ sulcal landscape to include four previously overlooked, small, shallow, and variable sulci. One of these sulci (ventral supralateral occipital sulcus, slocs-v) is present in nearly every hemisphere and is morphologically, architecturally, and functionally dissociable from neighboring sulci. A data-driven, model-based approach, relating sulcal depth to behavior further revealed that the morphology of only a subset of LPC/LPOJ sulci, including the slocs-v, is related to performance on a spatial orientation task.”

It is worth noting that we have added additional analyses that include the other three newly-characterized sulci in response to Reviewer 1. We first described the relationship between these sulci and demographic features, alongside analyses on the patterning of these sulci, which are included in the Results (Page 6):

“Beyond characterizing the incidence of sulci, it is also common in the neuroanatomical literature to qualitatively characterize sulci on the basis of fractionation and intersection with surrounding sulci (termed “sulcal types”; for examples in other cortical expanses, see Chiavaras & Petrides, 2000; Drudik et al., 2023; Miller et al., 2021; Paus et al., 1996; Weiner et al., 2014; Willbrand, Parker, et al., 2022). All four sulci most commonly did not intersect with other sulci (see Supplementary Tables 1-4 for a summary of the sulcal types of the slocs and pAngs dorsal and ventral components). The sulcal types were also highly comparable between hemispheres (rs > .99 , ps < .001). Though we characterize these sulci in this paper for the first time, the location of these four sulci is consistent with the presence of variable “accessory sulci” in this cortical expanse mentioned in prior modern and classic studies (Supplementary Methods). We could also identify these sulci in post-mortem hemispheres (Supplementary Figs. 2, 3), ensuring that these sulci were not an artifact of the cortical reconstruction process.

Given that sulcal incidence and patterning is also sometimes related to demographic features (Cachia et al., 2021; Leonard et al., 2009; Wei et al., 2017), subsequent GLMs relating the incidence and patterning of the three more variable sulci (slocs-d, pAngs-v, and pAngs-d) to demographic features (age and gender) revealed no associations for any sulcus (ps > .05).  Finally, to help guide future research on these newly- and previously-classified LPC/LPOJ sulci, we generated probabilistic maps of each of these 17 sulci and share them with the field with the publication of this paper (Supplementary Fig. 6; Data availability).”

- The tone of the article suggests a discovery of these 4 sulci when some of them have already been reported (as rightfully highlighted in the article), though not named nor studied specifically. This is slightly misleading as I interpret the first part of the article as a proposition of nomenclature rather than a discovery of sulci.

We have toned down our language throughout the paper, emphasizing that this paper is updating the sulcal landscape of LPC/LOPJ taking into account these sulci that have not been comprehensively described previously. For example, in the Abstract (Page 1), we now write:

“After defining thousands of sulci in a young adult cohort, we revised the previous LPC/LPOJ sulcal landscape to include four previously overlooked, small, shallow, and variable sulci. One of these sulci (ventral supralateral occipital sulcus, slocs-v) is present in nearly every hemisphere and is morphologically, architecturally, and functionally dissociable from neighboring sulci. A data-driven, model-based approach, relating sulcal depth to behavior further revealed that the morphology of only a subset of LPC/LPOJ sulci, including the slocs-v, is related to performance on a spatial orientation task. “

- The article never mentions the concept of merging of sulcal elements and the potential effect it could have on the labeling of the newly named variable sulci.

We emphasize that we use multiple surfaces (pial, inflated, smoothwm) to help distinguish intersecting sulci from one another. We include extra text in the Methods (Page 21):

“We defined LPC/LPOJ sulci for each participant based on the most recent schematics of sulcal patterning by Petrides (2019) as well as pial, inflated, and smoothed white matter (smoothwm) FreeSurfer cortical surface reconstructions of each individual. In some cases, the precise start or end point of a sulcus can be difficult to determine on a surface (Borne et al., 2020); however, examining consensus across multiple surfaces allowed us to clearly determine each sulcal boundary in each individual. “

Further, upon quantifying the patterning of these variable sulci, a majority of the time they are independent (described in the Results on Page 6):

“Beyond characterizing the incidence of sulci, it is also common in the neuroanatomical literature to qualitatively characterize sulci on the basis of fractionation and intersection with surrounding sulci (termed “sulcal types”; for examples in other cortical expanses, see (Chiavaras & Petrides, 2000; Drudik et al., 2023; Miller et al., 2021; Paus et al., 1996; Weiner et al., 2014; Willbrand, Parker, et al., 2022). All four sulci most commonly did not intersect with other sulci (see Supplementary Tables 1-4 for a summary of the sulcal types of the slocs and pAngs dorsal and ventral components). The sulcal types were also highly comparable between hemispheres (rs > .99 , ps < .001).”

Thus, merging sulcal elements likely had a minimal impact on the present definitions.

- The definition of the new sulci is solely based on their localization relative to other sulci which are themselves variable (e.g. the 3rd branch of the STS can show different locations and different orientation, potentially affecting the definition of the slocs-v). This is not addressed in the discussion.

As displayed in our probabilistic maps of these sulci (Supplementary Fig. 6), the cSTS components (2-4) are actually relatively consistent between individuals, and thus, future investigators can utilize these maps to help define these sulci in new hemispheres.

Nevertheless, there is, of course, individual variability in the location of these sulci, and we do agree that this point brought up by the Reviewer is important. We have now added text to the Limitations section of the Discussion (Pages 15-16):

“The main limitation of our study is that presently, the most accurate methodology to define sulci —especially the small, shallow, and variable PTS—requires researchers to manually trace each structure on the cortical surface reconstructions. This method is limited due to the individual variability of cortical sulcal patterning (Fig. 1, Supplementary Fig. 5), which makes it challenging to identify sulci, let alone PTS, without extensive experience and practice. However, we anticipate that our probabilistic maps  will provide a starting point and hopefully, expedite the identification of these sulci in new participants. This method is also arduous and time-consuming—which, on the one hand, limits the sample size in terms of number of participants, while on the other, results in thousands of precisely defined sulci. This push-pull  relationship reflects a broader conversation in the human brain mapping and cognitive neuroscience fields between a balance of large N studies and “precision imaging” studies in individual participants (Allen et al., 2022; Gratton et al., 2022; Naselaris et al., 2021; Rosenberg and Finn, 2022).”

- The new sulci are only defined in terms of localization relative to other sulci, and no other property is described (general length, depth, orientation, shape...), making it hard for a new observer to take labeling decisions in case of conflict.

To help guide future investigators, we now show these metrics for all sulci in Supplemental Figure 7 to help future groups identify these sulci with the assistance of their general morphology.

- The very assertive tone of the article conveys the idea that these sulci are identifiable certainly in most cases, when by definition these highly variable tertiary sulci are sometimes very difficult to take decisions on.

The highly variable nature of ¾ of the putative tertiary sulci (slocs-v, slocs-d, pAngs-v, pAngs-d) described here is why we focused on the slocs-v (as it is identifiable in nearly all f hemispheres). However, we have edited our language throughout the text to also emphasize the variability of these sulci. For example, in the Results (Page 5), we now write:

“In previous research in small sample sizes, neuroanatomists noticed shallow sulci in this cortical expanse (Supplementary Methods and Supplementary Figs. 1-4 for historical details). In the present study, we fully update this sulcal landscape considering these overlooked indentations. In addition to defining the 13 sulci previously described within the LPC/LPOJ, as well as the posterior superior temporal cortex (Methods) (Petrides, 2019) in individual participants, we could also identify as many as four small and shallow PTS situated within the LPC/LPOJ that were highly variable across individuals and uncharted until now (Supplementary Methods and Supplementary Figs. 1-4). Macroanatomically, we could identify two sulci between the cSTS3 and the IPS-PO/lTOS ventrally and two sulci between the cSTS2 and the pips/IPS dorsally. We focus our analyses on the slocs-v since it was identifiable in nearly every hemisphere.”

- I am not absolutely convinced with the labeling proposed of a previously reported sulcus, namely the posterior intermediate parietal sulcus.

In defining previously-identified LPC sulci, we followed the previous labeling procedure by Petrides (2019) alongside historical definitions (detailed in Supplementary Figures 1-4). Nevertheless, future deep learning algorithms using these and others data can be used to rectify discrepancies in labeling (e.g., Borne et al., 2020 Medical Image Analysis; Lyu et al., 2021 NeuroImage). We discuss these points in the Limitations section of the Discussion (Pages 16-17):

“The main limitation of our study is that presently, the most accurate methodology to define sulci —especially the small, shallow, and variable PTS—requires researchers to manually trace each structure on the cortical surface reconstructions. This method is limited due to the individual variability of cortical sulcal patterning (Fig. 1, Supplementary Fig. 5), which makes it challenging to identify sulci without extensive experience and practice. However, we anticipate that our probabilistic maps  will provide a starting point and hopefully, expedite the identification of these sulci in new participants. This should accelerate the process of subsequent studies confirming the accuracy of our updated schematic of LPC/LOPJ. This manual method is also arduous and time-consuming, which, on the one hand, limits the sample size in terms of number of participants, while on the other, results in thousands of precisely defined sulci. This push-pull relationship reflects a broader conversation in the human brain mapping and cognitive neuroscience fields between a balance of large N studies and “precision imaging” studies in individual participants (Allen et al., 2022; Gratton et al., 2022; Naselaris et al., 2021; Rosenberg & Finn, 2022). Though our sample size is comparable to other studies that produced reliable results relating sulcal morphology to brain function and cognition (e.g., (Cachia et al., 2021; Garrison et al., 2015; Lopez-Persem et al., 2019; Miller et al., 2021; Roell et al., 2021; Voorhies et al., 2021; Weiner, 2019; Willbrand, Parker, et al., 2022; Willbrand, Voorhies, et al., 2022; Yao et al., 2022), ongoing work that uses deep learning algorithms to automatically define sulci should result in much larger sample sizes in future studies (Borne et al., 2020; Lyu et al., 2021). Finally, the time-consuming manual definitions of primary, secondary, and PTS also limit the cortical expanse explored in each study, thus, restricting the present study to LPC/LPOJ. “

Assuming that the labelling of all sulci reported in the article is reproducible, the different results are convincing and in general, this study achieves its aims in defining more precisely the sulcation of the LPOJ and looking into its functional/cognitive value. This work clearly offers a finer understanding of sulcal pattern in this region, and lacks only little for the new markers to be convincingly demonstrated. An overall coherence of the labelling can still be inferred from the supplementary material which support the results and therefore the conclusions, yet, addressing some of the weaknesses listed above would greatly enhance the impact of this work. This work is important to the understanding of sulcal variability and its implications on functional and cognitive aspects.

We thank the Reviewer for their positive remarks on the implications of this work.

Reviewer #3 (Public Review):

Summary: 72 subjects, and 144 hemispheres, from the Human Connectome Project had their parietal sulci manually traced. This identified the presence of previously undescribed shallow sulci. One of these sulci, the ventral supralateral occipital sulcus (slocs-v), was then demonstrated to have functional specificity in spatial orientation. The discussion furthermore provides an eloquent overview of our understanding of the anatomy of the parietal cortex, situating their new work into the broader field. Finally, this paper stimulates further debate about the relative value of detailed manual anatomy, inherently limited in participant numbers and areas of the brain covered, against fully automated processing that can cover thousands of participants but easily misses the kinds of anatomical details described here.

Strengths:

- This is the first paper describing the tertiary sulci of the parietal cortex with this level of detail, identifying novel shallow sulci and mapping them to behaviour and function.

- It is a very elegantly written paper, situating the current work into the broader field.

- The combination of detailed anatomy and function and behaviour is superb.

We thank the Reviewer for their positive remarks on paper and our findings.

Weaknesses:

- The numbers of subjects are inherently limited both in number as well as in typically developing young adults.

We emphasize that the sample size is limited due to the arduous nature of manually defining sulci; however, we provide probabilistic maps with the publication of this work to help expedite this process for future investigators. Further, with improved deep learning algorithms, the sample sizes in future neuroanatomical studies should be enhanced. We discuss these points in the Limitations section of the Discussion (Pages 16-17):

“The main limitation of our study is that presently, the most accurate methodology to define sulci —especially the small, shallow, and variable PTS—requires researchers to manually trace each structure on the cortical surface reconstructions. This method is limited due to the individual variability of cortical sulcal patterning (Fig. 1, Supplementary Fig. 5), which makes it challenging to identify sulci without extensive experience and practice. However, we anticipate that our probabilistic maps  will provide a starting point and hopefully, expedite the identification of these sulci in new participants. This should accelerate the process of subsequent studies confirming the accuracy of our updated schematic of LPC/LOPJ. This manual method is also arduous and time-consuming, which, on the one hand, limits the sample size in terms of number of participants, while on the other, results in thousands of precisely defined sulci. This push-pull relationship reflects a broader conversation in the human brain mapping and cognitive neuroscience fields between a balance of large N studies and “precision imaging” studies in individual participants (Allen et al., 2022; Gratton et al., 2022; Naselaris et al., 2021; Rosenberg & Finn, 2022). Though our sample size is comparable to other studies that produced reliable results relating sulcal morphology to brain function and cognition (e.g., (Cachia et al., 2021; Garrison et al., 2015; Lopez-Persem et al., 2019; Miller et al., 2021; Roell et al., 2021; Voorhies et al., 2021; Weiner, 2019; Willbrand, Parker, et al., 2022; Willbrand, Voorhies, et al., 2022; Yao et al., 2022), ongoing work that uses deep learning algorithms to automatically define sulci should result in much larger sample sizes in future studies (Borne et al., 2020; Lyu et al., 2021). The time-consuming manual definitions of primary, secondary, and PTS also limit the cortical expanse explored in each study, thus restricting the present study to LPC/LPOJ.”

- While the paper begins by describing four new sulci, only one is explored further in greater detail.

Due to the increased variability of three of the four newly-classified sulci, we chose to only focus on the slocs-v given that it was present in nearly all hemispheres. In response to other reviewers, we have conducted additional analyses that also describe these new sulci and potential factors related to their incidence (Page 6):

“Given that sulcal incidence and patterning is also sometimes related to demographic features (Cachia et al., 2021; Leonard et al., 2009; Wei et al., 2017), subsequent GLMs relating the incidence and patterning of the three more variable sulci (slocs-d, pAngs-v, and pAngs-d) to demographic features (age and gender) revealed no associations for any sulcus (ps > .05).”

In addition, given that sulcal variability is cognitively (e.g., Amiez et al., 2018 Scientific Reports; Cachia et al., 2021 Frontiers in Neuroanatomy; Garrison et al., 2015 Nature Communications; Willbrand et al., 2022, 2023 Brain Structure & Function), anatomically (e.g., Amiez et al., 2021 Communications Biology; Vogt et al., 1995 Journal of Comparative Neurology), functionally (e.g., Lopez Persem et al., 2019 The Journal of Neuroscience), and translationally (e.g., Yucel et al., 2002 Biological Psychiatry) relevant, future research can investigate these relationships regarding the slocs-d and pAngs components. We have added text to the Limitations section of the Discussion (Pages 17-18) to discuss this:

“Finally, although we did not focus on the relationship between the other three PTS (slocs-d, pAngs-v, and pAngs-d) to anatomical and functional features of LPC and cognition, given that variability in sulcal incidence is cognitively (Amiez et al., 2018; Cachia et al., 2021; Garrison et al., 2015; Willbrand, Jackson, et al., 2023; Willbrand, Voorhies, et al., 2022), anatomically (Amiez et al., 2021; Vogt et al., 1995), functionally (Lopez-Persem et al., 2019), and translationally (Clark et al., 2010; Le Provost et al., 2003; Meredith et al., 2012; Nakamura et al., 2020; Yücel et al., 2002, 2003) relevant, future work can also examine the relationship between the more variable slocs-d, pAngs-v, and pAngs-d and these features.”

- There is some tension between calling the discovered sulci new vs acknowledging they have already been reported, but not named.

We have edited the manuscript throughout to emphasize our primary focus on revising the LPC/LOPJ sulcal landscape to include these often overlooked small, shallow, and variable putative tertiary sulci, rather than using the terms “discovered sulci” and “new.”

- The anatomy of the sulci, as opposed to their relation to other sulci, could be described in greater detail.

Beyond the radar plots in the main text which compare specific groupings of sulci, we now show the morphological metrics for all sulci investigated in the present work in Supplemental Figure 7.

Overall, to summarize, I greatly enjoyed this paper and believe it to be a highly valued contribution to the field.

We are glad the Reviewer enjoyed reading our paper and thank them for their positive thoughts on the potential impact of this work on the field.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The slocs-v is found in 71 subjects left and right. Is that the same subject?

No, these are different subjects.

(2) How were the 72 subjects chosen?

The subjects were randomly selected from the HCP database as describe in the methods (Page 18):

“Here, we used 72 randomly-selected participants, balanced for gender (following the terminology of the HCP data dictionary), from the HCP database (50% female, 22-36 years old, and 90% right-handed; there was no effect of handedness on our behavioral tasks; Supplementary materials) that were also analyzed in several prior studies (Hathaway et al., 2023; Miller et al., 2021, 2020; Willbrand et al., 2023b, 2023c, 2022a).”

(3) Are there effects of laterality on sulcal pattern? Table?

We now include sulcal pattern results in the Results section and Supplementary Materials; although there were no laterality effects regarding the sulcal pattern .

(4) Depiction/description of common sulcal patterns

We now include sulcal pattern results in the Results section and Supplementary Materials.

(5) Is there a relationship between sulcal patterns and demographic features?

We now include analyses on this in the Results section. There is no relationship between sulcal patterns and demographic features.

(6) Just for clarity, the sulcal features are studied and extracted in native space?

Yes, sulcal features are studied and extracted in native space, as described in the Methods section (Page 19):

“Anatomical T1-weighted (T1-w) MRI scans (0.8 mm voxel resolution) were obtained in native space from the HCP database. Reconstructions of the cortical surfaces of each participant were generated using FreeSurfer (v6.0.0), a software package used for processing and analyzing human brain MRI images (surfer.nmr.mgh.harvard.edu) (Dale et al., 1999; Fischl et al., 1999). All subsequent sulcal labeling and extraction of anatomical metrics were calculated from these native space reconstructions generated through the HCP’s version of the FreeSurfer pipeline (Glasser et al., 2013).”

(7) The authors use "Gender". Are they referring to biological sex (female/male) or socially defined characteristics (man/woman etc.)?

The term gender is referred to socially defined characteristics, as used by the HCP data dictionary (Methods page 18):

“Here, we used 72 randomly-selected participants, balanced for gender (following the terminology of the HCP data dictionary), from the HCP database (50% female, 22-36 years old, and 90% right-handed; there was no effect of handedness on our behavioral tasks; Supplementary materials) that were also analyzed in several prior studies (Hathaway et al., 2023; Miller et al., 2021, 2020; Willbrand et al., 2023b, 2023c, 2022a).”

(8) Fig 2. Grey is poorly visible compared to green and blue.

The shade of gray has been edited to be more distinguishable.

(9) The relationship between behavior and sulcal features is significant but weak.

We acknowledge that the morphological-behavioral relationship identified in the present study explains a modest amount of variance; however, the more important aspect of the finding is that multiple sulci identified in the model are recently-characterized sulci in LPC/LOPJ identified by our group and others (Petrides, 2019), and thus, the relationship would have been overlooked or lost if these sulci were not identified. We have added text to the Limitations section of the Discussion (Pages 17-18) to emphasize this point:

“It is also worth noting that the morphological-behavioral relationship identified in the present study explains a modest  amount of variance; however, the more important aspect of our findings is that multiple sulci identified in our model-based approach are recently-characterized sulci in LPC/LOPJ identified by our group and others (Petrides, 2019), and thus, the relationship would have been overlooked or lost if these sulci were not identified. “

(10) The Limitation section could be expanded.

We have added additional text to flesh out the Limitations section of the Discussion (Pages 17-18):

“It is also worth noting that the morphological-behavioral relationship identified in the present study explains a modest  amount of variance; however, the more important aspect of our findings is that multiple sulci identified in our model-based approach are recently-characterized sulci in LPC/LOPJ identified by our group and others (Petrides, 2019), and thus, the relationship would have been overlooked or lost if these sulci were not identified. Finally, although we did not focus on the relationship between the other three PTS (slocs-d, pAngs-v, and pAngs-d) to anatomical and functional features of LPC and cognition, given that variability in sulcal incidence is cognitively (Amiez et al., 2018; Cachia et al., 2021; Garrison et al., 2015; Willbrand, Jackson, et al., 2023; Willbrand, Voorhies, et al., 2022), anatomically (Amiez et al., 2021; Vogt et al., 1995), functionally (Lopez-Persem et al., 2019), and translationally (Clark et al., 2010; Le Provost et al., 2003; Meredith et al., 2012; Nakamura et al., 2020; Yücel et al., 2002, 2003) relevant, future work can also examine the relationship between the more variable slocs-d, pAngs-v, and pAngs-d and these features. “

Reviewer #2 (Recommendations For The Authors):

First, I would like to thank the authors for their important contribution to the field of sulcal studies and anatomo-functional correlates. My main comments about the work are treated in the public review, and I will only address details in this section. I have detected a number of typos which are harder to report from a document in which lines are not numbered. Could you please submit a numbered document for the next iteration?

- p2. "hominoid-specific, shallow indentations, or sulci" - can lead to misunderstanding that sulci are hominoid-specific and shallow

Sentence has been rewritten:

“Of all the neuroanatomical features to target, recent work shows that morphological features of the shallower, later developing, hominoid-specific indentations of the cerebral cortex (also known as putative tertiary sulci, PTS) are not only functionally and cognitively meaningful, but also are particularly impacted by multiple brain-related disorders and aging (Amiez et al., 2019, 2018; Ammons et al., 2021; Cachia et al., 2021; Fornito et al., 2004; Garrison et al., 2015; Harper et al., 2022; Hathaway et al., 2023; Lopez-Persem et al., 2019; Miller et al., 2021, 2020; Nakamura et al., 2020; Parker et al., 2023; Voorhies et al., 2021; Weiner, 2019; Willbrand et al., 2023b, 2023c, 2022a, 2022b; Yao et al., 2022).”

- p2. next sentence (starting with "The combination [...]": not clear that you are addressing tertiary sulci here, maybe introduce the concept beforehand?

The previous sentence (just above) has been edited to introduce putative tertiary sulci beforehand.

- p5. error in numbering of sulci relative to Fig1. (5,6,7,8 -> 6,7,8,9)

Sulcal numbering has been fixed.

-p5. reference to supp mat -> I would have expected the nomenclature used in Borne et al. 2020 to be discussed alongside with the state of the art. How would you relate F.I.P.r.int.1 and F.I.P.r.int.2 to the sulci you describe?

We thank the Reviewer for bringing up this relevant literature. The F.I.P.r.int. 1 and 2 are described as rami of the IPS, whereas the slocs and pAngs are independent, small indentations near the IPS, but not part of the complex. Nevertheless, future work should integrate these two schematics together to establish the most comprehensive sulcal map of LPC/LOPJ. We have added text to the Supplementary Methods detailing the differences between the F.I.P.r.int.1 and F.I.P.r.int.2 and slocs-/pAngs:

“slocs/pAng vs. F.I.P.r.int.1 and F.I.P.r.int.2

Recent work (Borne et al., 2020; Perrot et al., 2011) identified two intermediate rami of the IPS (F.I.P.r.int.1 and F.I.P.r.int.2) that were not defined in the present investigation. Crucially, the newly classified sulci here (slocs and pAngs) are distinguishable from the two F.I.P.r.int. in that the F.I.P.r.int. are branches coming off the main body of the IPS (Borne et al., 2020; Perrot et al., 2011), whereas the slocs/pAngs are predominantly non-intersecting (“free”) structures that never intersected with the IPS (Supplementary Tables 1-4).”

- p6. Fig 1.a. labelling discrepancy between line 1 and 2, column 4: the labels 10 and 11 from the inflated hemisphere do not match the labels 10 and 11 in the pial surface. Fig 1.b. swapped label 2 and 3 in the 4th hemisphere

These aspects of Figure 1 have been edited accordingly.

- p7. "(iii) the slocs-v was thicker than both the cSTS3 and lTOS" -> the slocs-v showed thicker gray matter?

The sentence has been adjusted (Page 7):

“(iii) the slocs-v showed thicker gray matter than both the cSTS3 and lTOS (ps < .001), “

- p9. Six left hemisphere LPC/LPOJ sulci were related to spatial orientation task performance -> missing

Fixed (Page 9):

“Six left hemisphere LPC/LPOJ sulci were related to spatial orientation task performance (Fig. 3a, b). “

- p14. "Steel and colleagues" -> missing space

Fixed (Page 14):

“Furthermore, the slocs-v appears to lie at the junction of scene-perception and place-memory activity (a transition that also consistently co-localizes with the HCP-MMP area PGp) as identified by Steel and colleagues (2021).”

- p20. Probability maps "we share these maps with the field" -> specify link to data availability

The link to data availability has been added (Page 21):

“To aid future studies interested in investigating LPC/LPOJ sulci, we share these maps with the field (Data availability). “

Reviewer #3 (Recommendations For The Authors):

No detailed recommendations not already present in the rest of the review.

Reviewer #1 (Public Review):

Summary:

This study investigates how the human brain flexibly adjusts its representations of the world as the environment continually changes. The authors identified regions where the representation continuously drifted across multiple months. They also found that the representation in the parahippocampal cortex could be rapidly influenced by recent environmental inputs.

Strengths:

(1) This study touches upon a crucial but less-explored issue: the relationship between semantic knowledge updating and representation drift in the brain.

(2) This study addresses this issue with a unique dataset in which participants viewed objects embedded in thousands of natural scenes across many fMRI sessions over eight months.

(3) The method for investigating whether the recent inputs could change the neural representation is compelling (i.e., subtracting the backward correlation value from the forward correlation value).

Weaknesses:

(1) Statistical Inference.

(a) Statistical inference is across eight subjects. Low statistical power means high false positive rates.

(b) Multiple comparisons across brain regions were not corrected.

(2) Object Encoding

It is unclear whether the identified brain regions represent the objects (as declared in the manuscript) or the visual features shared by pictures of similar items. Such visual features could be those of the background (e.g., spatial layout or the color tone of the scene), not the objects.

(3) Semantic Content in the MTL

Items with higher levels of semantic association tend to cooccur in the same picture. The results could be driven by the number of pictures shared between each pair of items, not semantic similarity (as declared in the manuscript).

(4) Long-term Drift of Item Representations in the MTL

(a) The results show a long-term representational drift in the brain but provide no evidence suggesting that this long-term neural representational drift reflects the drift in semantic representation. Although the authors used the "semantic" mask defined in the previous step, it does not mean the representation drift in the semantic mask is semantic, and there is doubt whether the "semantic" mask defined in the previous step is really semantic (see the third point).

(b) The beta value of the drift can not be directly compared across regions. Different regions have different sizes and signal-to-noise ratios in the BOLD signal. Their within-item similarity can not be compared directly in the first place.

(5) Recent Structure Rapidly Influences Item Representations in PHC

(a) It is unclear why the authors implement additional modularity analysis instead of directly using the pairwise co-occurrence frequencies among the 80 items, which is more straightforward.

(b) It does not make sense to compare the recent structure to the long-term structure across all 30 sessions because the structure of the posterior sessions cannot influence the current structure updating.

(c) It is unclear how the authors calculate the structure-induced change in the PHC in Figure 7.

eLife assessment

This valuable study investigates how the human brain flexibly adjusts its representations of the world as the environment continually changes. It utilizes a unique dataset in which participants view thousands of natural scenes across many fMRI sessions over multiple months. The evidence supporting the claims of the authors is incomplete, with statistical inference not always warranted. The study would interest a broad readership in cognitive neuroscience.

Reviewer #2 (Public Review):

Summary:

The authors set out to uncover which brain regions might support the continuous updating of semantic associations thereby showing a system of semantic plasticity. Using fMRI data from participants viewing thousands of natural scene images over 30 recording sessions, they hoped to establish how objects co-occuring with each other within images influences the semantic representations in the human brain that relate to those object concepts.

Strengths:

There is a lot to like about the paper. A major strength of the methods and results is the convincing demonstration of many of the results. This includes showing item representations in the ventral visual pathway and medial temporal lobes (MTL), as we would expect. They also show semantic effects - defined using the word co-occurrence vectors from word2vec, along the posterior and anterior ventral visual pathway and MTL - replicating various past studies. The authors use a creative approach to show that the item representations measured within each session are modulated by the co-occurrence structure in previous trials, becoming more closely related. And that item representations seem to subtly change over the course of the 30 sessions, in that they become less related to each other with increasing distance. However, the semantic effects within each session itself are claimed to remain unchanged.

Weaknesses:

This leads to what I see as a weakness in the study. The conclusions relate to semantic plasticity and the changes in semantic (associative) representations. The drift analyses do appear to show representational changes across the sessions, but this is based on the item representations. The inference is that this is due to an updating of knowledge about the associations each item has had with other items. Yet, in the same regions, the authors suggest that semantic associative effects, as tested using word2vec for each session, remain stable. Doesn't this seem to contradict the claims about semantic plasticity?

Some of this is difficult to unpick as the semantic stability analysis using word2vec in each session is only very briefly mentioned, and the data is not shown (I would include it). So, at present, I feel they show evidence of representational changes but do not show evidence of what the nature of the change is. If the neural representations consistently reflect the long-term semantic associations (which is what word2vec captures), then how does this combine with the drift effects of item representations?

Does it mean that the changes in item representations do not reflect semantic associative knowledge? And reflect some other non-specified type of information (perhaps as the participants are doing an image memory test).

Another potential weakness is the robustness of the drift analysis itself. For the drift analysis, item representations in each session are compared to all other sessions and then averaged according to the number of intervening sessions. This means the data for item representation with a session difference of 1 will be based on 29 data points, a session difference of 2 on 28 data points ... and a session difference of 29 based on 1 data point. So there is a huge imbalance in the amount of data that goes into the analysis for the different numbers of intervening sessions. This leads me to wonder if it could impact the validity of the results. An alternative might be to use 1 datapoint for each session (or a suitable value, I imagine 5 would still give enough data to analyse drifts) and calculate drift, and then repeat this with different partitions of the data to see how stable it is, and if drift is reliably occurring. Alternatively, the analyses they use might have been used and validated previously.

To be clear, I do think this is a very nice study and will have a positive impact on researchers interested in object processing, semantic knowledge, statistical learning, and schemas. But think there are some gaps between what the data shows evidence for, and the ultimate inferences made.

Reviewer #3 (Public Review):

Summary:

This study characterizes the relative stability of semantic representations in the human brain using functional magnetic resonance imaging (fMRI) data. The authors suggest that representations in the early stages of processing within the visual system are stable over hours, weeks, and months, while representations in later stages of processing - within the medial temporal lobe - change more rapidly, sometimes within the span of a single fMRI session.

To make this claim, the authors conduct a series of analyses using a well-established fMRI dataset. This begins with a decoding analysis to identify regions that contain reliable object-specific information. This approach identifies early stages within canonical visual cortices (e.g., primary visual cortex, V1), as well as downstream regions within the medial temporal lobe (MTL); this includes perirhinal cortex (PRC), parahippocampal cortex (PHC), and several subfields within the hippocampal cortex (e.g., CA1). Next, they identify regions that are correlated with "semantic features" associated with these objects, determined using word2vec embeddings of each of these object names. Several regions within the MTL (CA1, PRC, PHC) were significantly correlated with these word2vec embeddings. The authors then turn their analyses to representational change across two different timescales. Between scan sessions, regions at early stages of visual processing (e.g., V1) contain relatively stable representations, while regions within the MTL decreased their auto-correlation across sessions, suggesting that there is increased representational change/drift in the MTL. Finally, the authors demonstrate that there is representational change with PHC within a single scan session - changes that reflect the statistics of visual experiences.

Strengths:

The analyses conducted in this study are solid and creative and they yield compelling theoretical results. Beyond the paper's central claims, this study also highlights the utility of publicly available datasets (i.e., NSD) in exploring and evaluating novel theoretical ideas.

Especially compelling is the combined analysis used to estimate reliable item-level representations, first, and then the long-term drift of item representations (i.e., between sessions). The design choices for modeling the fMRI data (e.g., the cross-validated approach to predicting voxel-level responses) reflect state-of-the-art analysis methods, while the control regions used in these analyses (e.g., V1) provide compelling contrasts to the experimental effects. This makes it clear that the observed representational drift/instability is not present throughout the visual system. These results indicate that this effect is worthy of future experiments, while also providing auxiliary information related to effect size, etc.

Weaknesses:

The concerns outlined here do not challenge the central claim within this study, relating to the relative instability of representations within the MTL as compared to V1. Instead, these concerns focus on whether these representations should be described as "semantic," the importance we should give to the distinction between PHC and other MTC structures, and the lack of systematic analysis in relation to the "gradient" from posterior to anterior regions. In each case, I have provided suggestions as to how these concerns might be addressed. Finally, I've made a note about whether these data should be interpreted in terms of neural "plasticity" given the lack of behavioral change in relation to these fMRI data.

(1) No reason to believe that representations within the MTL are necessarily 'semantic.'

The authors suggest "evoked object representations in CA1, PHC, and PRC are semantic in nature." However, the correlation between fMRI responses and word2vec embeddings-the only evidence for "semantic" representations-is ambiguous. These structures might contain high-dimensional features that are associated with these objects for other reasons; concretely, there might be visual information that is not semantic but relates to the reliable visual properties of these objects (e.g., texture, shape, location in the image). Yet there are no analyses to disambiguate between these alternative accounts. As such, labeling these as "semantic" representations is suggestive but premature. Nonetheless, developing such a control analysis should be relatively straightforward. I outline one possible approach below.

While "semantic" information is a relatively nebulous term in the cognitive neurosciences, contemporary deep-learning methods might offer unambiguous ways to characterize such representations. If we assume that "semantics" relate to the meaning of an object/entity and not the "low-level" sensory attributes related to encoding this information, this leads to a straightforward implementation of object semantics: the reliable variance that can be isolated within the residuals of a sensory encoder. For example, do word2vec embeddings explain variance within the medial temporal lobe above and beyond the variance explained by a vision-only image encoder? Of course, care must be taken to use a visual encoder which is not itself a crystallization of object semantics (e.g., encoders optimized using a classification objective), but this is all very feasible given contemporary computer vision methods. Adding such a control analysis would offer a significant improvement over the current approach, clarifying the nature of the stimulus-driven representations within the medial temporal lobe by disentangling "semantic" properties of reliable visual features.

Additionally, it is not clear whether results from the current "object encoding" analysis and "semantic detection" analysis differ because of underlying differences in representational content in these regions or because of design choices in these analyses themselves. That is, while the object encoding analysis learns a linear projection from a one-hot 80-dimensional vector to hemodynamic responses in each brain region, the semantic detection analysis correlates these predicted hemodynamic responses with word2vec embeddings associated with each of these 80 objects. These different analysis methods result in different outcomes: not all regions identified by the object encoding analysis are also identified in the semantic detection analysis (e.g., hippocampal subfields). It is not clear to what degree these different outcomes are a function of "semantic" information, or are simply a consequence of differences in analytic approaches. It would be useful to know the results by repeating the logic from the object encoding analysis, but instead of 1-hot vectors for each object, use the word2vec embeddings.

(2) Unclear if the differences between PHC and other MTL structures are driven by SNR.

Parahippocampal cortex (PHC) is a region reliably identified by the analyses in this study: PHC is identified in the analysis of item encoding, semantic content, and representational drift across long (between-session) and short (within-session) timescales. Control regions here provide a convincing contrast to PHC in each of these analyses, and so the role of PHC appears clear in these analyses. However, it is unclear how to interpret the difference between PHC and other structures within the MTC - namely, the observation that PHC alone is influenced by representational drift across shorter timescales. It's possible that these effects are common throughout the MTL, but are only evident in PHC because of increased SNR. This concern seems plausible when observing PHC's "encoding success" and "semantic content," both visually and statistically, relative to other MTL structures: the magnitude of PHC's effect appears greater, which could simply be an artifact of PHC's relatively high SNR. In fMRI data, for example, PRC typically has relatively low SNR due to field inhomogeneities related to dropout, due to PRC's relative proximity to the ear canal-which is exacerbated in 7T (vs 3T) scanners, which was the case for the data in this study.

Addressing this concern could be relatively straightforward. For example, including information about the SNR in each respective brain region would be very helpful. If the SNR across brain regions within the MTL is relatively uniform, then this already addresses the concern above. regardless, it would be useful to report the experimental effects in relation, for example, the split-half reliability of signal in each brain region. That is, instead of simply reporting that that results are significant across brain regions, the authors might estimate how reliable the variance is across brain regions, and use this reliable variance as a ceiling which can be used to normalize the amount of variance explained in each analysis. By providing an account of the differences in the reliability/SNR of different regions, we would have a much better estimate of the relative importance of differences in the results reported for different regions within the MTL.

(3) Need for more systematic analysis/visualization of "posterior" vs. "anterior" regions.

The authors report that "Whole-brain analyses revealed a gradient of plasticity in the temporal lobe, with drift more evident in anterior than posterior areas." However, the only contrast provided in the main text is between MTL structures and V1-there is no "gradient" in any of these analyses. There are other regions visualized in Supplemental Figure 3, but there is not a systematic evaluation of the gradient along a "posterior/anterior" axis. It would be helpful to see the results in Figures 3A, 4A, 5A, and 6A to include other posterior visual regions (e.g., V4, LOC, PPA, FFA) beyond V1.

(4) Without behavioral data, not a direct relationship with "stability-plasticity tradeoff"

The results from this study are framed in relation to a "stability-plasticity tradeoff." As argued in this manuscript, this tradeoff is central to animal behavior - our ability to rapidly deploy prior knowledge to respond to the world around us. Given that there are no behavioral measures used in the current study, however, no claims can be made about how these fMRI data might relate to learning, or behavior more generally. As such, framing these results in terms of a stability-plasticity tradeoff is tenuous. "Representational drift," on the other hand, is a term that is relatively agnostic in its relationship with behavior, and aptly describes the results presented here. The authors refer to this term as well. Considering the lack of behavioral evidence, alongside the core findings from these neuroimaging data, "representational stability" or "representational "drift" seems to be a more direct description of the available data than "neural plasticity" or a "stability-plasticity tradeoff."

Author response:

We are very appreciative of the reviewers’ assessment that we used “solid and creative” methods to provide a “convincing demonstration” of “compelling theoretical results” on a “crucial but less-explored issue” in cognitive neuroscience. We are also grateful for their thoughtful suggestions for analyses and for pointing out areas where our analysis descriptions need more clarity. While we will respond to all comments in a future response and revision, here we provide information and clarification on a few central points.

Localization of semantic content:

Regarding our semantic analysis, one reviewer rightly pointed out that items with a high degree of semantic association, as captured by word2vec, tend to occur in the same images, and they expressed concern that this could drive our similarity results. We wish to clarify here (and will revise the manuscript accordingly) that we excluded all pairs of co-occurring items in our word2vec semantic analysis in order to avoid this issue. Thus, our results cannot be driven by the number of images within which items co-occurred. We also agree with the reviewer who stated that “semantic information” is a nebulous term in the cognitive neurosciences, and it appears to have led to some confusion as to the nature of our claims. We take a broad view of this term, with the perspective that visual features (e.g., color, shape) can contribute to semantic content rather than necessarily competing with it. In our work, we use word2vec to identify neural representations that reflect the kind of semantic content present in word embedding models—but the conclusions we draw do not depend on these representations being devoid of visual content. That is, we do not use word2vec to examine semantic versus visual representations, but rather to narrow down the set of representations to be considered in subsequent analyses. While there are a range of legitimate views on what should be considered a “semantic” representation, our broad view, which is inclusive of visual content, along with our strategy for localizing semantic content are both standardly used in the visual neuroscience literature. Prior work in this literature has compared the ability of word2vec and low-level visual models to predict neural responses to natural images and found that the brain regions in which activity is accurately predicted by the models are considerably distinct: whereas a low-level visual model best predicts activity in V1, V2, and V4, word2vec performs better in more anterior regions, including in visual areas such as lateral occipital cortex (Güçlü & van Gerven, 2015, arXiv). This suggests that our effects are unlikely to be explained by overlap in the kinds of low-level visual features mentioned by the reviewers. However, the semantic content we localize and the representation of high-level visual features may indeed overlap, and this is compatible with our claims. We will do more in our revision to be explicit about our intended meaning in our use of the word “semantic” and how our approach relates to and builds on prior work in this literature.

Long-term representational drift:

We want to clarify our claims regarding the representational drift analysis. One reviewer stated that, while we show evidence of representational drift, we “provide no evidence suggesting that this long-term neural representational drift reflects a drift in semantic representation.” Another reviewer said: “The inference is that this [drift] is due to an updating of knowledge about the associations each item has had with other items,” and that our finding that semantic structure remains stable within these regions seems “to contradict the claims about semantic plasticity.” The claim we intended to make, which will be unpacked more clearly in our revision, is that the neural representations underlying semantic content drift over time, even if the semantic content itself is unchanging. In other words, we do not claim that our across-session drift analyses show changes in knowledge about object associations. Indeed, one of the reasons that representational drift has recently captured the attention of neuroscientists is that the neural representations underlying certain behaviors or cognitive content appear to drift over time even when the behaviors or cognitive content remain fixed. The relational structure of the neural representations can remain stable, even if the particular neurons recruited to represent each stimulus change over time (see, e.g., the T-maze in Rule, O’Leary, & Harvey., 2019, Curr Opin Neurobiol). Here we are translating these ideas, which were developed using animal models and/or primarily focused on low-level vision, to the semantic system in humans. The neural representations we identify in our paper capture semantic information because they share a similarity structure with word2vec, and the level of similarity to word2vec remains stable over time. Thus, our findings provide a simple demonstration of long-term representational drift in the human semantic system akin to that reported in animals—drift in the neural semantic representations of items even as the relations between these item representations appear stable.

Signal-to-noise variability across the MTL:

A reviewer raised the possibility that differences between our ROIs could be driven by variability in signal-to-noise ratio (SNR) across regions, particularly within the medial temporal lobe (MTL). We looked at noise ceiling SNR brain maps for each participant, which reflect the reliability of neural responses across repetitions of the same image. Preliminary analyses indicate that SNR differences do not account for our object encoding, semantic content, representational drift, or short-term plasticity measures across the MTL.

eLife assessment

This valuable paper presents convincing evidence that changing the constraint of how long to stop at an intermediate target significantly influences the degree of coarticulation of two sequential reaching movements, as well as their response to mechanical perturbations. Using an optimal-control framework, the authors offer a normative explanation of how both co-articulated and separated sequential movement can be understood as an optimal solution to the task requirements.

Reviewer #1 (Public Review):

In their paper, Kalidini et al. investigate why the motor system sometimes coarticulates movements within a sequence. They begin by examining this phenomenon in an optimal feedback controller (OFC) that performs reaching movements to two targets (T1 and T2). They show that coarticulation occurs only when the controller is not required to slow down at T1. When the controller must decelerate at T1, coarticulation does not occur. This observation holds true even though the controller has information about both targets in both scenarios. They test the same experiment on human participants and show that humans also coarticulate the reaches only when they are instructed to treat the first target as a via point. Both in human participants and OFC simulations, whenever the coarticulation is present, the long-latency response to perturbations during the first reach is also informed by the second target- suggesting that the information about the second target is already present in the circuitry that control the long-latency reflex.<br /> All experiments and analyses are standard and clearly explained. Their analysis of long-latency as a measure of coarticulation of sequence items is highly interesting and broadly useful for future experiment design. They successfully demonstrate that one reason the motor system sometimes coarticulates movements is due to high-level instructions on how to execute the sequence. These high-level instructions can, in turn, determine how and to what extent information about future sequence items is utilized by the low-level controller that governs muscle activity. However, the precise interaction between high-level task demands and low-level controllers at the neural tissue level remains an open question.

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript the authors examine the question of whether discrete action sequences and coarticulated continuous sequential actions can be produced from the same controller, without having to derive separate control policies for each sequential movement. Using modeling and behavioral experiments, the authors demonstrate that this is indeed possible if the constraints of the policy are appropriately specified. These results are of interest to those interested in motor sequences, but it is unclear whether these findings can be interpreted to apply to the control of sequences more broadly (see weaknesses below).

Strengths:<br /> The authors provide an interesting and novel extension of the stochastic optimal control model to demonstrate how different temporal constraints can lead to either individual or coarticulated movements. The authors use this model to make predictions about patterns of behavior (e.g., in response to perturbations), which they then demonstrate in human participants both by measuring movement kinematics as well as EMG. Together this work supports the authors' primary claims regarding how changes in task instructions (i.e., task constraints) can result in coarticulated or separated movement sequences and the extent to which the subsequent movement goal affects the planning and control of the previous movement.

Weaknesses:<br /> Although this work is quite interesting, it remains unknown whether there is a fundamental distinction between a coarticulated sequence and a single movement passing through a via point (or equivalently, avoiding an obstacle). The notion of a coarticulated sequence brings with it the notion of sequential (sub)movements and temporal structure, whereas the latter can really be treated as more of a constraint on the production of a single continuous movement. The authors suggest that these are not truly different kinds of movements at the level of a control policy, but this remains to be tested experimentally.

It also remains unclear for the theory of optimal feedback control as a whole where and how the cost function and constraints are specified to guide the optimization process. That is, presumably there is the ability for higher-level or explicit description of these constraints, but how they then become incorporated into a control policy remains unclear. With regard to the kind of multi-target constraints proposed here, in typical sequence tasks, while some movements become coarticulated, people also tend to form chunks with distinct chunk boundaries. This presumably means that there is at least some specification of the sequential ordering of these chunks that must exist beyond the control policy and that multiple control policies may still be warranted to execute an entire sequence (otherwise the authors' model might suggest that people can coarticulate forever without needing to exhibit any chunk boundaries). Hence, while the authors fairly convincingly show that a single control policy can lead to separated or coarticulated movements given an appropriate set of constraints, their work does not speak to where or how those constraints are specified, nor to how longer sequences are controlled.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary: 

In this paper, Kalidindi and Crevecoeur ask why sequential movements are sometimes coarticulated. To answer this question, first, they modified a standard optimal controller to perform consecutive reaches to two targets (T1 and T2). They investigated the optimal solution with and without a constraint on the endpoint's velocity in the via target (T1). They observed that the controller coarticulates the movements only when there is no constraint on the speed at the via-point. They characterized coarticulation in two ways: First, T2 affected the curvature of the first reach in unperturbed reaches. Second, T2 affected corrective movements in response to a mechanical perturbation of the first reach. 

Parallel to the modeling work, they ran the same experiment on human participants. The participants were instructed to either consider T1 as via point (go task) or to slow down in T1 and then continue to T2 (stop task). Mirroring the simulation results, they observed coarticulation only in the go task. Interestingly, in the go task, when the initial reach was occasionally perturbed, the long-latency feedback responses differed for different T2 targets, suggesting that the information about the final target was already present in the motor circuits that mediate the long-latency response. In summary, they conclude that coarticulation in sequential tasks depends on instruction, and when coarticulation happens, the corrections in earlier segments of movement reflect the entirety of the coarticulated sequence.

Evaluation 

Among many strengths of this paper, most notably, the results and the experiment design are grounded in, and guided by the optimal control simulation. The methods and procedures are appropriate and standard. The results and methods are explained sufficiently and the paper is written clearly. The results on modulation of long-latency response based on future goals are interesting and of broad interest for future experiments on motor control in sequential movement. However, I find the authors' framing of these results, mostly in the introduction section, somewhat complicated.

The current version of the introduction motivates the study by suggesting that "coarticulation and separation of sub-movement [in sequential movements] have been formulated as distinct hypotheses" and this apparent distinction, which led to contradictory results, can be resolved by Optimal Feedback Control (OFC) framework in which task-optimized control gains control coarticulation. This framing seems complicated for two main reasons. First, the authors use chunking and coarticulation interchangeably. However, as originally proposed by (Miller 1956), the chunking of the sequence items may fully occur at an abstract level like working memory, with no motoric coarticulation of sequence elements at the level of motor execution. In this scenario, sequence production will be faster due to the proactive preparation of sequence elements. This simple dissociation between chunking and coarticulation may already explain the apparent contradiction between the previous works mentioned in the introduction section. Second, the authors propose the OFC as a novel approach for studying neural correlates of sequence production. While I agree that OFC simulations can be highly insightful as a normative model for understanding the importance of sequence elements, it is unclear to me how OFCs can generate new hypotheses regarding the neural implementation of sequential movements. For instance, if the control gains are summarizing the instruction of the task and the relevance of future targets, it is unclear in which brain areas, or how these control gains are implemented. I believe the manuscript will benefit from making points more clear in the introduction and the discussion sections. 

We agree that chunking may occur at different levels that do not necessarily involve motor coarticulation. We clarified that our contribution is towards answering why sequence movements sometimes coarticulate, and how the way sequences are executed influences the representation of future goals in the sensorimotor system.

To address this point, we made the following modifications in the introduction:

Line 44:

“It remains unclear how future goals are integrated in the sensorimotor system. For rapid execution of a sequence, one possible solution is to represent multiple goals within low-level control circuits (3, 16), enabling the execution of several elements as a single entity, called “motor chunk”. Note that chunking can also occur at a higher level such as in working memory-guided sequences, which in this case may or may not involve the production of a movement (17, 18).”

Lines 50:

“Recent neural recordings in the primary motor cortex (M1) have shown no specific influence of future goals on the population responses governing ongoing action (19, 20). Specifically, Zimnik and Churchland (20) observed in a two-reach sequence task that, there was no coarticulation in sub-movement kinematics although the execution got faster with practice. Notably, M1 displayed separate phases of execution related activity for each sub-movement. Using a neural network model, they interpreted that sequence goals could be separated and serially specified to the controller from regions upstream of M1 (Figure 1A). These findings contrast with earlier studies showing coarticulation of sub-movements and whole sequence representations in M1 (21–23). As a result, it has been suggested that coarticulation and separation in rapid sequences may involve distinct computations: coarticulation possibly involves replacing sub-movements with a motor chunk, while separation possibly indicates independent control of each sub-movement with chunking at a higher-level (4, 20).  Thus, there are unresolved questions regarding why sequential movements sometimes coarticulate, and how the representation of future goals in the sensorimotor system influences the way sequences are executed.”

With respect to the second part of your concern about OFC, we agree that this framework does not make direct prediction about the neural implementation and our statements required clarifications. The first link between the model and prediction about neural data follows from the observation that long-latency circuits participate in task-dependent sequence production, thus indicating that transcortical pathways must express this task dependency. The second link between our work and neural activities is by providing a counter argument to previous interpretation: indeed, Zimnik and Churchland argued that independent or “holistic” sequence production should be associated with different representations in monkey’s brain. In contrast we suggest that the same controller can flexibly generate both kinds of sequences, without implying a different structure in the controller, only a different cost-function. We thus refine the expectation about neural correlates of sequence representations by showing that it potentially relates to the encoding of task constraints.

To address this point, we added the following changes in the introduction and discussion:

Line 69 in Introduction: 

“The theory of optimal feedback control (OFC) has been particularly useful in predicting the influence of numerous task parameters on the controller (27–34), thus reproducing goal-directed motor commands during both unperturbed movements and feedback responses to disturbances (30). OFC has been used in numerous studies to interpret flexible feedback responses occurring in the long-latency response period (30, 35).” 

Line 454 in Discussion:

“Although OFC has been predominantly used as a behavioral level framework agnostic to neural activity patterns, it can shed light on the planning, state estimation and execution related computations in the transcortical feedback pathway (Takei et al.,). Using OFC, our study proposes a novel and precise definition of the difference to expect in neural activities in order to identify coarticulated versus independent sequence representations from a computational point of view. Because each condition (i.e., overlapping versus non-overlapping controllers as in Figure 2) was associated with different cost-functions and time-varying control gains, it is the process of deriving these control gains, using the internal representation of the task structure, that may differ across coarticulated and separated sequence conditions. To our knowledge, how and where this operation is performed is unknown. A corollary of this definition is that the preparatory activity (20, 50) may not discern independently planned or coarticulated sequences because these situations imply different control policies (and cost functions), as opposed to different initial states. Moreover, the nature of the sequence representation is potentially not dissociable from its execution for the same reason.”

Reviewer #2 (Public Review):

Summary: 

In this manuscript, the authors examine the question of whether discrete action sequences and coarticulated continuous sequential actions can be produced from the same controller, without having to derive separate control policies for each sequential movement. Using modeling and behavioral experiments, the authors demonstrate that this is indeed possible if the constraints of the policy are appropriately specified. These results are of interest to those interested in motor sequences, but it is unclear whether these findings can be interpreted to apply to the control of sequences more broadly (see weaknesses below). 

Strengths: 

The authors provide an interesting and novel extension of the stochastic optimal control model to demonstrate how different temporal constraints can lead to either individual or coarticulated movements. The authors use this model to make predictions about patterns of behavior (e.g., in response to perturbations), which they then demonstrate in human participants both by measuring movement kinematics as well as EMG. Together this work supports the authors' primary claims regarding how changes in task instructions (i.e., task constraints) can result in coarticulated or separated movement sequences and the extent to which the subsequent movement goal affects the planning and control of the previous movement. 

Weaknesses: 

I reviewed a prior version of this manuscript, and appreciate the authors addressing many of my previous comments. However, there are some concerns, particularly with regard to how the authors interpret their findings. 

We thank the reviewer for their continued assessment of our work and for helping us to improve the paper. We are convinced that this and the previous review helped us clarifying our work considerably.

(1) It would be helpful for the authors to discuss whether they think there is a fundamental distinction between a coarticulated sequence and a single movement passing through a via point (or equivalently, avoiding an obstacle). The notion of a coarticulated sequence brings with it the notion of sequential (sub)movements and temporal structure, whereas the latter can be treated as more of a constraint on the production of a single continuous movement. If I am interpreting the authors' findings correctly it seems they are suggesting that these are not truly different kinds of movements at the level of a control policy, but it would be helpful for the authors to clarify this claim. 

Indeed, this is our interpretation of the results/simulations. This suggestion can also be observed in Ramkumar et al., article on chunking. To clarify this, we added a statement in the discussion as follows: 

Line 449: 

“Notably, in the framework of optimal feedback control, an intermediate goal is equivalent to a via-point that constrains the execution of the sequence (similar to (13)). It is thus possible that coarticulation in motor systems be processed similarly as other kinds of movement constraints, such as via-points, avoiding obstacles, or changes in control policies.”

(2) The authors' model clearly shows that each subsequent target only influences the movement of one target back, but not earlier ones (page 7 lines 199-204). This stands in contrast to the paper they cite from Kashefi 2023, in which those authors clearly show that people account for at least 2 targets in the future when planning/executing the current movement. It would be useful to know whether this distinction arises because of a difference in experimental methodology, or because the model is not capturing something about human behavior.  

Thank you for raising this point. There are some differences between the study of Kashefi and colleagues (2023), and ours. Both studies looked into planning of more than one reach. In the study of Kashefi et al., the results of Figure 6 showed that in H2 condition, there was no significant curvature, and the curvature increases in H3 and H4 conditions (only in the 75ms dwell-time scenario). Note that H2 condition in their work meant the presentation of +2 target after the initiation of +1 reach. Hence, we think the GO task in our case should be compared to the H3 condition, resulting in similar curvature as in our study. These authors also showed that curvature increased even in the H4 condition (75 ms dwell). OFC also accommodates this observation, if we consider the relationship between the cost of intermediate goals and spatial location of the targets (see figure below, also added to Supplementary Figure 4). To see this, we performed additional 3 target simulations where the constraint on intermediate goal velocity (at T1 and T2) was varied to achieve similar dwell velocity at the intermediate targets (Supplementary Figure 4C). In this case, the hand curvature of the first reach differed while the dwell velocity was similar across T3 up and T3 down conditions, as may be instructed experimentally. Again, the task instructions and the spatial location of the future goals together determine how much the first reach components are influenced by the next ones, and this may impact several reaches ahead. 

We added the following clarification in the result to describe this. 

Line 199:

“It is worth noting that the OFC model can be generalized to longer sequences (10) through the incorporation of additional cost terms (in Equation 10 of Methods) and targets, enabling simultaneous planning for more than two targets. Simulations of a sample three-reach sequence (Supplementary Figure S4) revealed that, varying the cost of dwell velocity at intermediate targets (w2 and w3 parameters in Methods) caused a variation in control gains. Different amount of change in control gains can be expected for intermediate versus late targets (Supplementary Figure 4A). Notably, even when we used the same dwell velocity cost (w2 = w3 = 0), the observed velocity profiles were different between the two sequences towards different final targets (T3 up and T3 down) (Supplementary Figure 4B). We tested a condition in which both sequence reaches were forced to have similar dwell velocity profiles by increasing the dwell velocity costs in the sequence towards one of the targets (T3 down), while leaving this parameter unchanged for the other target (T3 up). In this scenario, T3 up sequence had the parameters (w2, w3) = (0, 0), while T3 down sequence had the parameters (0.8, 0.8). In this case, the curvature of the first reach was different, and predominantly occurred due to differences in K2 between the two sequence reaches (Supplementary Figure S4C). These simulations highlight that, planning for a longer horizon sequence can indirectly influence the curvature of early reaches, due to the interaction between intermediate dwell constraints, spatial arrangement of targets, and sequence horizon in a task dependent manner.”

(3) In my prior review I raised a concern that the authors seem to be claiming that because they can use a single control policy for both coarticulated and separated movement sequences, there need not be any higher-level or explicit specification of whether the movements are sequential. While much of that language has been removed, it still appears in a few places (e.g., p. 13, lines 403-404). As previously noted, the authors' control policy can generate both types of movements as long as the proper constraints are provided to the model. However, these constraints must be specified somewhere (potentially explicitly, as the authors do by providing them as task instructions). Moreover, in typical sequence tasks, although some movements become coarticulated, people also tend to form chunks with distinct chunk boundaries, which presumably means that there is at least some specification of the sequential ordering of these chunks that must exist (otherwise the authors' model might suggest that people can coarticulate forever without needing to exhibit any chunk boundaries). Hence the authors should limit themselves to the narrow claim that a single control policy can lead to separated or coarticulated movements given an appropriate set of constraints, but acknowledge that their work cannot speak to where or how those constraints are specified in humans (i.e., that there could still be an explicit sequence representation guiding coarticulation). 

We thank the reviewer for raising this point. We do not dispute the statement that the controller needs to be set dependent on the constraints of the task that must be specified somewhere. In our view, this problem is similar to the question of how a cost-function (or a task representation) is transformed into a control policy in the brain, which is unknown in general. In the earlier version, our intention was to stress that separation can occur without necessarily implying that the goals be processed independently (as in Figure 1A and Zimnik 2021). To avoid confusion on this point, we modified this statement in the new version as follows:

Line 405: 

“A straightforward interpretation could be that the stopping at the first target invoked a completely different strategy in which the control of the two reaches was performed independently (Figure 1A), effectively separating the two movements, whereas executing them rapidly could produce the merging of the two sub-movements into a coarticulated sequence. While this is conceptually valid, it is not necessary and the model provides a more nuanced view: both apparent separation or coarticulation of the two motor patterns can be explained within the same framework of flexible feedback control. These different modes of sequence execution still require proper specification of the task constraints in the model, such as number of intermediate steps, dwell-time, or velocity limit. Such specifications must be considered as input to the controller.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Line 57: Distinct hypotheses. 

Line 209, The term "planned holistically" is confusing here. Seems like the authors suggest that the sequence is "planned holistically" as long as all sequence elements are given during the optimization process. 

We changed the sentence as follows.

Line 218: 

“Overall, the model predicted that even if a feedback control policy was computed by optimizing the whole sequence over a long time-horizon, the requirements associated with intermediate goals determine how early in the sequence the second (future) target can influence the feedback controller”

Line 336, It was not clear to me why the authors explained "the weak significant" results of PEC shortening in R0 given the nonsignificant values in R1. 

We wanted to be transparent about whether changing the statistical analysis will lead to different interpretations, such as the sequence encoding even before long latency epochs. But we realized that it could lead to confusion and we deleted this sentence in the updated manuscript.

Reviewer #2 (Recommendations For The Authors): 

About Weakness #2, to clarify this point the authors should either model and discuss what it would take for their model to account for multiple targets ahead, or else run a study to show that in this task people indeed only ever plan 1 target ahead.  

Please see our response above (in Weakness #2).

I am still puzzled by why people would resist the perturbation more when they eventually have to move in the direction of the perturbation (e.g., p 10 lines 313-314). Perhaps this is simply due to the geometry of the task, but it could also depend on what participants were trying to accomplish in the experiment. To help clarify this, the authors should report exactly what instructions were given to participants in each task condition.  

The simulations suggest that the observed perturbation movements are an optimal way to perform the task given the task constraints on accuracy, control effort and constraints at intermediate goals. The intuition is that modulating the acceleration at the intermediate goal is preferred rather than missing it. This however depends on the cost parameter. 

Below, in Author response figure 1, we show the simulations by varying the accuracy requirements at intermediate goal and the total motor cost parameters. Clearly, as expected, increasing the cost on accuracy of the intermediate reach, or decreasing the cost on motor output modulated the hand deviation (simulations not included in the article).

Author response image 1.

Impact of movement costs (motor effort and intermediate goal reach errors) on the hand path following a mechanical perturbation   

Our observation suggests that participants’ behaviour agreed with the interpretation that can result from the model. We clarified the exact instructions in the methods section. Note that the instructions were given at the beginning of the task and did not differ across the different conditions involving changes in the location of T2 or perturbation direction:

Line 594:

Participants were given the following instructions verbally: “Wait in the starting circle until you receive a GO signal, where the target circles turn red and you will simultaneously hear a beep sound. When the circles turn red, react quickly, move as soon, and as straight as possible to target 1 and then move to target 2. You will get two points at the end of the trial if you reach T1 in the prescribed time window and then move to T2, and in all other cases you will not receive any points. Importantly, once you reach T1 you should try to come out of it quickly. If you stay in T1 for more than 150 ms then T2 will disappear and you will receive only one point. Additionally, in some trials, a force will perturb your hand towards the right or left direction randomly while moving towards T1. The instructions remain the same in the presence of perturbations. Try to score as many points as you can.”

Additionally, we added the following lines in the results description:

Line 284:

“The influence of second target on the lateral hand deviation was qualitatively similar to that observed in model simulations, and counterintuitive to what we might expect without the help of the model simulations. As observed in the model simulations (see also Supplementary Figure S2), lateral hand deviation was smaller when the perturbation was in the direction of the second target (T2) and vice-versa. This was consistent for both rightward and leftward perturbation conditions. Both the model and humans expressed this strategy that can be seen as an emergent feature of efficient feedback control during production of movement sequences. Additionally, even though behavior was reproduced in simulations, changing the cost on control effort and/or accuracy of intermediate reaches could modulate the sequencedependent changes in curvature.”

I am not sure if "the data and code for simulations can be provided by the corresponding author" satisfies the eLife/PLoS software guidelines (i.e., that it be deposited in a public repository).

Thank you for pointing this out. This sentence was added by mistake.

We modified this statement in the updated manuscript. 

“The data and code from simulations and experiments is available in the public repository ‘figshare’ in the following link (https://figshare.com/s/865a8b77c264ef17a181).”

Reviewer #1 (Public Review):

Summary:

The authors sought to investigate the associations of age at breast cancer onset with the incidence of myocardial infarction (MI) and heart failure (HF). They employed a secondary data analysis of the UK Biobank. They used descriptive and inferential analysis including Cox proportional hazards models to investigate the associations. Propensity score matching was also used. They found that Among participants with breast cancer, younger onset age was significantly associated with elevated risks of MI (HR=1.36, 95%CI: 1.19 to 1.56, P<0.001) and HF (HR=1.31, 95% CI: 1.18 to 1.46, P<0.001). the reported similar findings after propensity matching.

Strengths:

The use of a large dataset is a strength of the study as the study is well-powered to detect differences. Reporting both the unmatched and the propensity-matched estimates was also important for statistical inference.

Weaknesses:

The authors have addressed all my previous comments. I have no further comments.

eLife assessment

In this valuable study, the authors sought to investigate the associations of age at breast cancer onset with the incidence of myocardial infarction and heart failure. Based on results from a series of compelling statistical analyses, the authors conclude that a younger onset age of breast cancer is associated with myocardial infarction and heart failure, highlighting the need to carefully monitor the cardiovascular status of women who have been diagnosed with breast cancer.

Author response:

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

Response to Reviewer #1:

Comment 1:

Summary:

The authors sought to investigate the associations of age at breast cancer onset with the incidence of myocardial infarction (MI) and heart failure (HF). They employed a secondary data analysis of the UK Biobank. They used descriptive and inferential analysis including Cox proportional hazards models to investigate the associations. Propensity score matching was also used. They found that Among participants with breast cancer, younger onset age was significantly associated with elevated risks of MI (HR=1.36, 95%CI: 1.19 to 1.56, P<0.001) and HF (HR=1.31, 95% CI: 1.18 to 1.46, P<0.001). the reported similar findings after propensity matching.

Strengths:

The use of a large dataset is a strength of the study as the study is well-powered to detect differences. Reporting both the unmatched and the propensity-matched estimates was also important for statistical inference.

Weaknesses:

Despite the merits of the paper, readers may get confused as to whether authors are referring to “age at breast cancer onset” or “age at breast cancer diagnosis”. I suppose the title refers to the latter, in which case it will be best to be consistent in using “age at breast cancer diagnosis” throughout the manuscripts. I would recommend a revision to the title to make it explicit that the authors are referring to “age at breast cancer diagnosis”.

Thank you for your nice comments and suggestions. Yes, as you mentioned, in this study, we focused on age at breast cancer diagnosis, which was obtained from the cancer registry data in the UK Biobank and was used in all the analyses. We agree with you that it would be better to consistently use “age at diagnosis of breast cancer” throughout the manuscripts for a better understanding; therefore, we have replaced “age at breast cancer onset” with “age at diagnosis of breast cancer”.

Change in the manuscript:

“Age at breast cancer onset” was replaced with “age at diagnosis of breast cancer” in the title and throughout the manuscripts.

Recommendations For The Authors:

Kindly review the references for the location of the full stop. Putting the full stop at the end of the parenthesis makes reading smother than its current form as it is difficult to know when the new sentence begins.

Thank you for your suggestion. We have made revisions to the location of the full stop next to a reference.

Change in the manuscript:

The full stop was put at the end of the parenthesis of a reference throughout the manuscripts.

Response to Reviewer #2:

Comment 1:

This is a well-presented large analysis from the UK Biobank of nearly 250,000 female adults. The authors examined the associations of breast cancer diagnosis with incident myocardial infarction and heart failure by different onset age groups. Based on results from a series of statistical analyses, the authors concluded that younger onset age of breast cancer was associated with myocardial infarction and heart failure, highlighting the necessity of careful monitoring of cardiovascular status in women diagnosed with breast cancer, especially those younger ones.

Comments to consider:

It’s thoughtful for the authors to have included and adjusted for menopausal status, breast cancer surgery, and hormone replacement therapy in their sensitivity analysis. It would be informative if the authors presented the number and percentages of menopause and cancer treatments.

Thank you for your comments. As suggested, we have provided more detailed information on the number and percentage of menopausal status and breast cancer treatments.

Change in the manuscript:

Page 11, Lines 208 to 211: added “Among participants with breast cancer, 11 460 (70.6%) participants were postmenopausal, 14 255 (87.6%) participants had undergone breast cancer surgery, and 6 784 (41.8%) participants had received hormone replacement therapy.”

Change in the supplementary material:

The number and percentage of menopausal status, breast cancer surgery, and hormone replacement therapy were added to Table S13.

aAdjusted for age, ethnicity, education, current smoking, current drinking, obesity, exercise, low-density lipoprotein cholesterol, depressed mood, hypertension, diabetes, antihypertensive drug use, antidiabetic drug use, statin use, menopausal status, breast cancer surgery, and hormone replacement therapy.

HR, hazard ratio; CI, confidence interval.

Comment 2:

The analytical baseline used for follow-up should be pointed out in the methods section. It’s confusing whether the analytic baseline was defined as the study baseline or the time at breast cancer diagnosis.

We apologize for the confusion. In this study, the analytical baseline used for follow-up was defined as the baseline of UK Biobank (2006-2010) and we have pointed it out in the methods section as suggested.

Change in the manuscript:

Page 9, Lines 165 to 166: added: “The analytical baseline used for follow-up was defined as the baseline of UK Biobank (2006-2010).”

Comment 3:

Did the older onset age group have a longer follow-up duration? Could the authors provide information on the length of follow-up by age of onset in Supplementary Table S4? It would give the readers more information regarding different age groups.

Thank you for your question. We compared the time of follow-up among the three diagnosis age groups and found that although the durations of follow-up among the three groups were quite similar (as shown in Table S4), statistical analysis revealed a significant difference with the older diagnosis age group demonstrating a longer follow-up duration (P for Kruskal-Wallis test <0.001). This is understandable as with large sample sizes, even a slight difference could lead to statistical significance. According to your suggestion, we have added information on the length of follow-up by age of diagnosis in Supplementary Table S4.

Change in the supplementary material:

Added the median and interquartile range of follow-up in Supplementary Table S4.

The results are presented as the mean ± standard deviation, or No. (%).

aThe effect sizes are standardized mean differences for continuous outcomes and the Phi coefficient for dichotomous outcomes.

LDL-C, low-density lipoprotein cholesterol.

Reviewer #3 (Public Review):

Summary:

Bell and colleagues studied how different splice isoforms of voltage-gated CaV2 calcium channels affect channel expression, localization, function, synaptic transmission, and locomotor behavior at the larval Drosophila neuromuscular junction. They reveal that one mutually exclusive exon located in the fourth transmembrane domain encoding the voltage sensor is essential for calcium channel expression, function, active zone localization, and synaptic transmission. Furthermore, a second mutually exclusive exon residing in an intracellular loop containing the binding sites for Caβ and G-protein βγ subunits promotes the expression and synaptic localization of around ~50% of CaV2 channels, thereby contributing to ~50% of synaptic transmission. This isoform enhances release probability, as evident from increased short-term depression, is vital for homeostatic potentiation of neurotransmitter release induced by glutamate receptor impairment, and promotes locomotion. The roles of the two other tested isoforms remain less clear.

Strengths:

The study is based on solid data that was obtained with a diverse set of approaches. Moreover, it generated valuable transgenic flies that will facilitate future research on the role of calcium channel splice isoforms in neural function.

Weaknesses:

(1) Based on the data shown in Figures 2A-C, and 2H, it is difficult to judge the localization of the cac isoforms. Could they analyze cac localization with regard to Brp localization (similar to Figure 3; the term "co-localization" should be avoided for confocal data), as well as cac and Brp fluorescence intensity in the different genotypes for the experiments shown in Figure 2 and 3 (Brp intensity appears lower in the dI-IIA example shown in Figure 3G)? Furthermore, heterozygous dIS4B imaging data (Figure 2C) should be quantified and compared to heterozygous cacsfGFP/+.

(2) They conclude that I-II splicing is not required for cac localization (p. 13). However, cac channel number is reduced in dI-IIB. Could the channels be mis-localized (e.g., in the soma/axon)? What is their definition of localization? Could cac be also mis-localized in dIS4B? Furthermore, the Western Blots indicate a prominent decrease in cac levels in dIS4B/+ and dI-IIB (Figure 1D). How do the decreased protein levels seen in both genotypes fit to a "localization" defect? Could decreased cac expression levels explain the phenotypes alone?

(3) Cac-IS4B is required for Cav2 expression, active zone localization, and synaptic transmission. Similarly, loss of cac-I-IIB reduces calcium channel expression and number. Hence, the major phenotype of the tested splice isoforms is the loss of/a reduction in Cav2 channel number. What is the physiological role of these isoforms? Is the idea that channel numbers can be regulated by splicing? Is there any data from other systems relating channel number regulation to splicing (vs. transcription or post-transcriptional regulation)?

(4) Although not supported by statistics, and as appreciated by the authors (p. 14), there is a slight increase in PSC amplitude in dIS4A mutants (Figure 2). Similarly, PSC amplitudes appear slightly larger (Figure 3J), and cac fluorescence intensity is slightly higher (Figure 3H) in dI-IIA mutants. Furthermore, cac intensity and PSC amplitude distributions appear larger in dI-IIA mutants (Figures 3H, J), suggesting a correlation between cac levels and release. Can they exclude that IS4A and/or I-IIA negatively regulate release? I suggest increasing the sample size for Canton S to assess whether dIS4A mutant PSCs differ from controls (Figure 2E). Experiments at lower extracellular calcium may help reveal potential increases in PSC amplitude in the two genotypes (but are not required). A potential increase in PSC amplitude in either isoform would be very interesting because it would suggest that cac splicing could negatively regulate release.

(5) They provide compelling evidence that IS4A is required for the amplitude of somatic sustained HVA calcium currents. However, the evidence for effects on biophysical properties and activation voltage (p. 13) is less convincing. Is the phenotype confined to the sustained phase, or are other aspects of the current also affected (Figure 2J)? Could they also show the quantification of further parameters, such as CaV2 peak current density, charge density, as well as inactivation kinetics for the two genotypes? I also suggest plotting peak-normalized HVA current density and conductance (G/Gmax) as a function of Vm. Could a decrease in current density due to decreased channel expression be the only phenotype? How would changes in the sustained phase translate into altered synaptic transmission in response to AP stimulation?

(6) Why was the STED data analysis confined to the same optical section, and not to max. intensity z-projections? How many and which optical sections were considered for each active zone? What were the criteria for choosing the optical sections? Was synapse orientation considered for the nearest neighbor Cac - Brp cluster distance analysis? How do the nearest-neighbor distances compare between "planar" and "side-view" Brp puncta?

(7) Cac clusters localize to the Brp center (e.g., Liu et al., 2011). They conclude that Cav2 localization within Brp is not affected in the cac variants (p. 8). However, their analysis is not informative regarding a potential offset between the central cac cluster and the Brp "ring". Did they/could they analyze cac localization with regard to Brp ring center localization of planar synapses, as well as Brp-ring dimensions?

(8) Given the accelerated PSC decay/ decreased half width in dI-IIA (Fig. 5Q), I recommend reporting PSC charge in Figure 3, and PPR charge in Figures 5A-D. The charge-based PPRs of dI-IIA mutants likely resemble WT more closely than the amplitude-based PPR. In addition, miniature PSC decay kinetics should be reported, as they may contribute to altered decay kinetics. How could faster cac inactivation kinetics in response to single AP stimulation result in a decreased PSC half-width? Is there any evidence for an effect of calcium current inactivation on PSC kinetics? On a similar note, is there any evidence that AP waveform changes accelerate PSC kinetics? PSC decay kinetics are mainly determined by GluR decay kinetics/desensitization. The arguments supporting the role of cac splice isoforms in PSC kinetics outlined in the discussion section are not convincing and should be revised.

(9) Paired-pulse ratios (PPRs): On how many sweeps are the PPRs based? In which sequence were the intervals applied? Are PPR values based on the average of the second over the first PSC amplitudes of all sweeps, or on the PPRs of each sweep and then averaged? The latter calculation may result in spurious facilitation, and thus to the large PPRs seen in dI-IIB mutants (Kim & Alger, 2001; doi: 10.1523/JNEUROSCI.21-24-09608.2001).

(10) Could the dI-IIB phenotype be simply explained by a decrease in channel number/ release probability? To test this, I propose investigating PPRs and short-term dynamics during train stimulation at lower extracellular Ca2+ concentration in WT. The Ca2+ concentration could be titrated such that the first PSC amplitude is similar between WT and dI-IIB mutants. This experiment would test if the increased PPR/depression variability is a secondary consequence of a decrease in Ca2+ influx, or specific to the splice isoform.

(11) How were the depression kinetics analyzed? How many trains were used for each cell, and how do the tau values depend on the first PSC amplitude? Time constants in the range of a few (5-10) milliseconds are not informative for train stimulations with a frequency of 1 or 10 Hz (the unit is missing in Figure 5H). Also, the data shown in Figures 5E-K suggest slower time constants than 5-10 ms. Together, are the data indeed consistent with the idea that dI-IIB does not only affect cac channel number, but also PPR/depression variability (p. 9)?

(12) The GFP-tagged I-IIA and mEOS4b-tagged I-IIB cac puncta shown in Figure 6N appear larger than the Brp puncta. Endogenously tagged cac puncta are typically smaller than Brp puncta (Gratz et al., 2019). Also, the I-IIA and I-IIB fluorescence sometimes appear to be partially non-overlapping. First, I suggest adding panels that show all three channels merged. Second, could they analyze the area and area overlap of I-IIA and I-IIB with regard to each other and to Brp, and compare it to cac-GFP? Any speculation as to how the different tags could affect localization? Finally, I recommend moving the dI-IIA and dI-IIB localization data shown in Figure 6N to an earlier figure (Figure 1 or Figure 3).

Author response:

eLife assessment

Cav2 voltage-gated calcium channels play key roles in regulating synaptic strength and plasticity. In contrast to mammals, invertebrates like Drosophila encode a single Cav2 channel, raising questions on how diversity in Cav2 is achieved from a single gene. Here, the authors present convincing evidence that two alternatively spliced isoforms of the Cac gene (cacophony, also known as Dmca1A and nightblindA) enable diverse changes in Cav2 expression, localization, and function in synaptic transmission and plasticity. These valuable findings will be of interest to a variety of researchers.

We suggest replacing “two alternatively spliced isoforms of the Cac gene” by “two alternatively spliced mutually exclusive exon pairs of the Cac gene”. 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Bell et. al. describes an analysis of the effects of removing one of two mutually exclusive splice exons at two distinct sites in the Drosophila CaV2 calcium channel Cacophony (Cac). The authors perform imaging and electrophysiology, along with some behavioral analysis of larval locomotion, to determine whether these alternatively spliced variants have the potential to diversify Cac function in presynaptic output at larval neuromuscular junctions. The author provided valuable insights into how alternative splicing at two sites in the calcium channel alters its function.

Strengths:

The authors find that both of the second alternatively spliced exons (I-IIA and I-IIB) that are found in the intracellular loop between the 1st and 2nd set of transmembrane domains can support Cac function. However, loss of the I-IIB isoform (predicted to alter potential beta subunit interactions) results in 50% fewer channels at active zones and a decrease in neurotransmitter release and the ability to support presynaptic homeostatic potentiation. Overall, the study provides new insights into Cac diversity at two alternatively spliced sites within the protein, adding to our understanding of how regulation of presynaptic calcium channel function can be regulated by splicing.

Weaknesses:

The authors find that one splice isoform (IS4B) in the first S4 voltage sensor is essential for the protein's function in promoting neurotransmitter release, while the other isoform (IS4A) is dispensable. The authors conclude that IS4B is required to localize Cac channels to active zones. However, I find it more likely that IS4B is required for channel stability and leads to the protein being degraded, rather than any effect on active zone localization. More analysis would be required to establish that as the mechanism for the unique requirement for IS4B.

We agree that we need to explain more clearly why IS4B is unlikely required for channel stability, but instead, likely has a unique function at the presynaptic active zone of fast synapses. We will address this by revising text and by providing additional data. If IS4B was required for evoked release because it supported channel protein stability, then the removal of IS4B should cause protein degradation throughout all sub-neuronal compartments and throughout the CNS, but this is not the case. First, upon removal of IS4B in adult motoneurons (which use cac channels at the presynapse and somatodendritically, Ryglewski et al., 2012) evoked release from axon terminals is abolished (as at the larval NMJ), but somatodendritic cac inward current is present. If IS4B was required for cac channel stability, somatodendritic current should also be abolished. We will add these data to the ms. Second, immunohistochemistry for tagged IS4B channels reveals that these are present not only at presynaptic active zones at the NMJ but also throughout the VNC motor neuropils. Excision of IS4B causes the absence of cac channels from the presynaptic active zones at the NMJ and throughout the VNC neuropils (and accordingly this is lethal). By contrast, tagged IS4A channels (with IS4B excised) are not found at the presynaptic terminals of fast synapses, but instead, in other distinct parts of the CNS. We will also provide data to show this. Together these data are in line with a unique requirement of IS4B at presynaptic active zones (not excluding additional functions of IS4B), whereas IS4A containing cac isoforms mediate different functions.

We appreciate the additional reviewer suggestions to the authors that we will address point by point when revising the ms. 

Reviewer #2 (Public Review):

This study by Bell et al. focuses on understanding the roles of two alternatively spliced exons in the single Drosophila Cav2 gene cac. The authors generate a series of cac alleles in which one or the other mutually exclusive exons are deleted to determine the functional consequences at the neuromuscular junction. They find alternative splicing at one exon encoding part of the voltage sensor impacts the activation voltage as well as localization to the active zone. In contrast, splicing at the second exon pair does not impact Cav2 channel localization, but it appears to determine the abundance of the channel at active zones. Together, the authors propose that alternative splicing at the Cac locus enables diversity in Cav2 function generated through isoform diversity generated at the single Cav2 alpha subunit gene encoded in Drosophila.

Overall this is an excellent, rigorously validated study that defines unanticipated functions for alternative splicing in Cav2 channels. The authors have generated an important toolkit of mutually exclusive Cac splice isoforms that will be of broad utility for the field, and show convincing evidence for distinct consequences of alternative splicing of this single Cav2 channel at synapses. Importantly, the authors use electrophysiology and quantitative live sptPALM imaging to determine the impacts of Cac alternative splicing on synaptic function. There are some outstanding questions regarding the mechanisms underlying the changes in Cac localization and function, and some additional suggestions are listed below for the authors to consider in strengthening this study. Nonetheless, this is a compelling investigation of alternative splicing in Cav2 channels that should be of interest to many researchers.

We agree that some additional information on cac isoform localization (in particular for splicing at the IS4 site) will strengthen the manuscript. We will address this by providing additional data and revising text (see responses to reviewers 1 and 3). We are also grateful for the additional reviewer suggestions which we will address point by point when revising the ms.  

Reviewer #3 (Public Review):

Summary:

Bell and colleagues studied how different splice isoforms of voltage-gated CaV2 calcium channels affect channel expression, localization, function, synaptic transmission, and locomotor behavior at the larval Drosophila neuromuscular junction. They reveal that one mutually exclusive exon located in the fourth transmembrane domain encoding the voltage sensor is essential for calcium channel expression, function, active zone localization, and synaptic transmission. Furthermore, a second mutually exclusive exon residing in an intracellular loop containing the binding sites for Caβ and G-protein βγ subunits promotes the expression and synaptic localization of around ~50% of CaV2 channels, thereby contributing to ~50% of synaptic transmission. This isoform enhances release probability, as evident from increased short-term depression, is vital for homeostatic potentiation of neurotransmitter release induced by glutamate receptor impairment, and promotes locomotion. The roles of the two other tested isoforms remain less clear.

Strengths:

The study is based on solid data that was obtained with a diverse set of approaches. Moreover, it generated valuable transgenic flies that will facilitate future research on the role of calcium channel splice isoforms in neural function.

Weaknesses:

(1) Based on the data shown in Figures 2A-C, and 2H, it is difficult to judge the localization of the cac isoforms. Could they analyze cac localization with regard to Brp localization (similar to Figure 3; the term "co-localization" should be avoided for confocal data), as well as cac and Brp fluorescence intensity in the different genotypes for the experiments shown in Figure 2 and 3 (Brp intensity appears lower in the dI-IIA example shown in Figure 3G)? Furthermore, heterozygous dIS4B imaging data (Figure 2C) should be quantified and compared to heterozygous cacsfGFP/+.

We understand the reviewer’s comment and will do the following to convincingly demonstrate absence of cac from presynaptic active zones upon IS4B excision. First, we will show selective enlargements of IS4A and IS4B with Brp in presynaptic active zones to show distinct cac label in active zones following excision of IS4A but not following excision of IS4B. Second, we will provide Pearson’s co-localization coefficients of Brp with IS4B and with IS4A, respectively. Third, we will reduce the intensity of the green channels in figures 2C and 2H to the same levels as in 2A and B, and H control to allow a fair comparison of cac intensities following excision of IS4B versus excision of IS4A and control. We had increased intensity to show that following excision of IS4B, no distinct cac label is found in active zones, even at high exaggerated image brightness. However, we agree with the reviewer that the bright background hampers interpretation and thus will show the same intensity in all images that need to be compared.

(2) They conclude that I-II splicing is not required for cac localization (p. 13). However, cac channel number is reduced in dI-IIB. Could the channels be mis-localized (e.g., in the soma/axon)? What is their definition of localization? Could cac be also mis-localized in dIS4B? Furthermore, the Western Blots indicate a prominent decrease in cac levels in dIS4B/+ and dI-IIB (Figure 1D). How do the decreased protein levels seen in both genotypes fit to a "localization" defect? Could decreased cac expression levels explain the phenotypes alone?

We will precisely define channel localization, and we will explain why it is highly unlikely that the absence of IS4B channels as well as the lower number of I-IIA channels are simply a consequence of reduced expression, but instead of splice variant specific channel function and localization. For example, upon excision of IS4B no cac channels are found at the presynaptic active zones and these synapses are thus non-functional. The isoforms containing the mutually exclusive IS4A exon are expressed and mediate other functions (see also response to reviewer 1) but cannot substitute IS4B containing isoforms at the presynapse. In fact, our Western blots are in line with reduced cac expression if all isoforms that mediate evoked release are missing, again indicating that the presynapse specific cac isoforms cannot be replaced by other cac isoforms (see also below, response to (3)). Feedback mechanisms that regulate cac expression in the absence of presynapse specific cac isoforms are beyond the scope of this study.

(3) Cac-IS4B is required for Cav2 expression, active zone localization, and synaptic transmission. Similarly, loss of cac-I-IIB reduces calcium channel expression and number. Hence, the major phenotype of the tested splice isoforms is the loss of/a reduction in Cav2 channel number. What is the physiological role of these isoforms? Is the idea that channel numbers can be regulated by splicing? Is there any data from other systems relating channel number regulation to splicing (vs. transcription or post-transcriptional regulation)?

We will provide additional evidence that mutually exclusive splicing at the IS4 site results in cac channels that localize to the presynaptic active zone (IS4B) versus cac channels that localize to other brain parts and/or other subneuronal compartments (see response to reviewer 1).  In addition, we already show in figure 2J that IS4B is required for normal cac HVA current, and we can add data showing that IS4A is not essential for cac HVA current. Similarly, for I-II we find it unlikely that differential splicing regulates channel numbers, but rather splice variant specific functions in different brain parts and different sub-neuronal compartments. To substantiate this interpretation, we will add data from developing adult motoneurons showing that excision of I-IIA causes reduced activity induced calcium influx into dendrites (new data), but it does not reduce channel number at the larval NMJ (figure 4). In our opinion these data are not in line with the idea that splicing regulates cac expression levels, and this in turn, results in specific defects in distinct neuronal compartments. However, we agree that the lack of isoforms with specific functions results in altered overall cac expression levels as indicated by our Western data. If isoforms normally abundantly expressed throughout most neuropils are missing due to exon excision, we indeed find less cac protein in Westerns. By contrast, the lack of isoforms with little abundance has little effect on cac expression levels. This may be the results of unknown feedback mechanisms which are beyond the scope of this study.

(4) Although not supported by statistics, and as appreciated by the authors (p. 14), there is a slight increase in PSC amplitude in dIS4A mutants (Figure 2). Similarly, PSC amplitudes appear slightly larger (Figure 3J), and cac fluorescence intensity is slightly higher (Figure 3H) in dI-IIA mutants. Furthermore, cac intensity and PSC amplitude distributions appear larger in dI-IIA mutants (Figures 3H, J), suggesting a correlation between cac levels and release. Can they exclude that IS4A and/or I-IIA negatively regulate release? I suggest increasing the sample size for Canton S to assess whether dIS4A mutant PSCs differ from controls (Figure 2E). Experiments at lower extracellular calcium may help reveal potential increases in PSC amplitude in the two genotypes (but are not required). A potential increase in PSC amplitude in either isoform would be very interesting because it would suggest that cac splicing could negatively regulate release.

There are several possibilities to explain this, but as none of the effects are statistically significant, we prefer to not investigate this in depth. However, given that we cannot find IS4A at the presynaptic active zone, IS4A is unlikely to have a direct negative effect on release probability. Nonetheless, given that IS4A containing cac isoforms mediate functions in other neuronal compartments it may regulate release indirectly by affecting action potential shape. We will provide data in response to the more detailed suggestions to authors that will provide additional insight.

(5) They provide compelling evidence that IS4A is required for the amplitude of somatic sustained HVA calcium currents. However, the evidence for effects on biophysical properties and activation voltage (p. 13) is less convincing. Is the phenotype confined to the sustained phase, or are other aspects of the current also affected (Figure 2J)? Could they also show the quantification of further parameters, such as CaV2 peak current density, charge density, as well as inactivation kinetics for the two genotypes? I also suggest plotting peak-normalized HVA current density and conductance (G/Gmax) as a function of Vm. Could a decrease in current density due to decreased channel expression be the only phenotype? How would changes in the sustained phase translate into altered synaptic transmission in response to AP stimulation?

Most importantly, HVA current is mostly abolished upon excision of IS4B (not IS4A, we think the reviewer accidentally mixed up the genotype). This indicates that the cac isoforms that mediate evoked release encode HVA channels. However, the somatodendritic current shown in figure 2J that remains upon excision of IS4B is mediated by IS4A containing cac isoforms. Please note that these never localize to the presynaptic active zone, thus the small inactivating HVA that remains in figure 2J does normally not mediate evoked release. Therefore, the interpretation is that specifically HVA current encoded by IS4B cac isoforms is required for synaptic transmission. Reduced cac current density is not the cause for this phenotype because a specific current component is absent. 

We agree with the reviewer that a deeper electrophysiological analysis of cac currents mediated by IS4B containing isoforms will be instructive. However, a precise analysis of activation and inactivation voltages and kinetics suffers form space clamp issues in recordings from the soma of such complex neurons (DLM motoneurons of the adult fly). Therefore, we will analyze the currents in a heterologous expression system and present these data to the scientific community as a separate study at a later time point.

(6) Why was the STED data analysis confined to the same optical section, and not to max. intensity z-projections? How many and which optical sections were considered for each active zone? What were the criteria for choosing the optical sections? Was synapse orientation considered for the nearest neighbor Cac - Brp cluster distance analysis? How do the nearest-neighbor distances compare between "planar" and "side-view" Brp puncta?

Max. z-projections would be imprecise because they can artificially suggest close proximity of label that is close in x and y but far away in z. Therefore, the analysis was executed in xy-direction of various planes of entire 3D image stacks. We considered active zones of different orientations (Fig. 4C, D). In fact, we searched the entire z-stacks until we found active zones of all orientations shown in figures 4C1-C6 within the same boutons. The same active zone orientations were analyzed for all exon-out mutants with cac localization in active zones. The distance between cac and brp did not change if viewed from the side.

(7) Cac clusters localize to the Brp center (e.g., Liu et al., 2011). They conclude that Cav2 localization within Brp is not affected in the cac variants (p. 8). However, their analysis is not informative regarding a potential offset between the central cac cluster and the Brp "ring". Did they/could they analyze cac localization with regard to Brp ring center localization of planar synapses, as well as Brp-ring dimensions?

In the top views (planar) we did not find any clear offset in cac orientation to brp between genotypes. This study focuses on cac splice isoform specific localization and function. Possible effects of different cac isoforms on Brp-ring dimensions or other aspects of scaffold structure are not central to our study, in particular given that Brp puncta are clearly present even if cac is absent from the synapse (Fig. 2H), indicating that cac is not instructive for the formation of the Brp scaffold.  

(8) Given the accelerated PSC decay/ decreased half width in dI-IIA (Fig. 5Q), I recommend reporting PSC charge in Figure 3, and PPR charge in Figures 5A-D. The charge-based PPRs of dI-IIA mutants likely resemble WT more closely than the amplitude-based PPR. In addition, miniature PSC decay kinetics should be reported, as they may contribute to altered decay kinetics. How could faster cac inactivation kinetics in response to single AP stimulation result in a decreased PSC half-width? Is there any evidence for an effect of calcium current inactivation on PSC kinetics? On a similar note, is there any evidence that AP waveform changes accelerate PSC kinetics? PSC decay kinetics are mainly determined by GluR decay kinetics/desensitization. The arguments supporting the role of cac splice isoforms in PSC kinetics outlined in the discussion section are not convincing and should be revised.

We agree that reporting charge in figure 3 will be informative and will do so. We also understand the reviewer’s concern attributing altered PSC kinetics to presynaptic cac channel properties. We will tone down our interpretation in the discussion and list possible alterations in presynaptic AP shape or Cav2 channel kinetics as alternative explanations (not conclusions). Moreover, we will quantify postsynaptic GluRIIA abundance to test whether altered PSC kinetics are caused by altered GluRIIA expression. In our opinion, the latter is more instructive than mini decay kinetic analysis because this depends strongly on the distance of the recording electrode to the actual site of transmission in these large muscle cells.

(9) Paired-pulse ratios (PPRs): On how many sweeps are the PPRs based? In which sequence were the intervals applied? Are PPR values based on the average of the second over the first PSC amplitudes of all sweeps, or on the PPRs of each sweep and then averaged? The latter calculation may result in spurious facilitation, and thus to the large PPRs seen in dI-IIB mutants (Kim & Alger, 2001; doi: 10.1523/JNEUROSCI.21-24-09608.2001).

We agree that the PP protocol and analyses have to be described more precisely in the methods, and we will do so. PPR values are based on the PPRs of each sweep and then averaged. We are aware of the study of Kim and Alger 2001, but it does not affect our data interpretation because all genotypes were analyzed identically, but only the I-IIB excision resulted in the large data spread shown in figure 5.

(10) Could the dI-IIB phenotype be simply explained by a decrease in channel number/ release probability? To test this, I propose investigating PPRs and short-term dynamics during train stimulation at lower extracellular Ca2+ concentration in WT. The Ca2+ concentration could be titrated such that the first PSC amplitude is similar between WT and dI-IIB mutants. This experiment would test if the increased PPR/depression variability is a secondary consequence of a decrease in Ca2+ influx, or specific to the splice isoform.

In fact, the interpretation that decreased PSC amplitude upon I-IIB excision is caused mainly by reduced channel number is precisely our interpretation (see discussion page 14, last paragraph to page 15, first paragraph). In addition, we are grateful for the reviewer’s suggestion to triturate the external calcium such that the first PSC amplitude matches the one in ΔI-IIB to test whether altered short term plasticity is solely a function of altered channel number or whether additional causes, such as altered channel properties, also play into this. We will conduct these experiments and include them in the revised manuscript.

(11) How were the depression kinetics analyzed? How many trains were used for each cell, and how do the tau values depend on the first PSC amplitude? Time constants in the range of a few (5-10) milliseconds are not informative for train stimulations with a frequency of 1 or 10 Hz (the unit is missing in Figure 5H). Also, the data shown in Figures 5E-K suggest slower time constants than 5-10 ms. Together, are the data indeed consistent with the idea that dI-IIB does not only affect cac channel number, but also PPR/depression variability (p. 9)?

For each animal, the amplitudes of each PSC were plotted over time and fitted with a single exponential. For depression at 1 and 10 Hz, we used one train per animal, and 5-6 animals per genotype (as reflected in the data points in Figs 5H and 5L). Given that the tau values are highly similar between control and excision of I-IIA, but ΔI-IIA tends to have larger single PSC amplitudes, differences in first PSC amplitude do not seem to skew the data (but see also response to comment 10 above). We thank the reviewer for pointing out that tau values in the range of ms are not informative at 1 and 10 Hz stimulations (Figs 5H and 5L). We mis-labeled (or did not label) the axes. The label should read seconds, not milliseconds. We apologize, and this will be corrected accordingly.

In sum, pending the outcome of additional important control experiments for GluRIIA abundance (see response to comment 8) and trituration of control PSC amplitude for the first pulse of paired pulses in ΔI-IIB (see response to comment 10) we will either modify or further support that interpretation.

(12) The GFP-tagged I-IIA and mEOS4b-tagged I-IIB cac puncta shown in Figure 6N appear larger than the Brp puncta. Endogenously tagged cac puncta are typically smaller than Brp puncta (Gratz et al., 2019). Also, the I-IIA and I-IIB fluorescence sometimes appear to be partially non-overlapping. First, I suggest adding panels that show all three channels merged. Second, could they analyze the area and area overlap of I-IIA and I-IIB with regard to each other and to Brp, and compare it to cac-GFP? Any speculation as to how the different tags could affect localization? Finally, I recommend moving the dI-IIA and dI-IIB localization data shown in Figure 6N to an earlier figure (Figure 1 or Figure 3).

We will show panels with all three labels matched as suggested by the reviewer. For the size of the puncta: this could be different numbers and types of fluorophores on the different antibodies used and thus different point spread, chromatic aberration, different laser and detector intensities etc. We will re-analyze the data to test whether there are systematic differences in size. We do not want to speculate whether the different tags have any effect on localization precision because of the abovementioned reasons as well as artificial differences in localization precision that can be suggested by different antibodies. We prefer to not move the figure because we believe it is informative to show our finding that active zones usually contain both splice variants together with the finding that only one splice variant is required for PHP.

eLife assessment

Cav2 voltage-gated calcium channels play key roles in regulating synaptic strength and plasticity. In contrast to mammals, invertebrates like Drosophila encode a single Cav2 channel, raising questions on how diversity in Cav2 is achieved from a single gene. Here, the authors present convincing evidence that two alternatively spliced isoforms of the Cac gene (cacophony, also known as Dmca1A and nightblindA) enable diverse changes in Cav2 expression, localization, and function in synaptic transmission and plasticity. These valuable findings will be of interest to a variety of researchers.

Reviewer #1 (Public Review):

Summary:

The manuscript by Bell et. al. describes an analysis of the effects of removing one of two mutually exclusive splice exons at two distinct sites in the Drosophila CaV2 calcium channel Cacophony (Cac). The authors perform imaging and electrophysiology, along with some behavioral analysis of larval locomotion, to determine whether these alternatively spliced variants have the potential to diversify Cac function in presynaptic output at larval neuromuscular junctions. The author provided valuable insights into how alternative splicing at two sites in the calcium channel alters its function.

Strengths:

The authors find that both of the second alternatively spliced exons (I-IIA and I-IIB) that are found in the intracellular loop between the 1st and 2nd set of transmembrane domains can support Cac function. However, loss of the I-IIB isoform (predicted to alter potential beta subunit interactions) results in 50% fewer channels at active zones and a decrease in neurotransmitter release and the ability to support presynaptic homeostatic potentiation. Overall, the study provides new insights into Cac diversity at two alternatively spliced sites within the protein, adding to our understanding of how regulation of presynaptic calcium channel function can be regulated by splicing.

Weaknesses:

The authors find that one splice isoform (IS4B) in the first S4 voltage sensor is essential for the protein's function in promoting neurotransmitter release, while the other isoform (IS4A) is dispensable. The authors conclude that IS4B is required to localize Cac channels to active zones. However, I find it more likely that IS4B is required for channel stability and leads to the protein being degraded, rather than any effect on active zone localization. More analysis would be required to establish that as the mechanism for the unique requirement for IS4B.

Reviewer #2 (Public Review):

This study by Bell et al. focuses on understanding the roles of two alternatively spliced exons in the single Drosophila Cav2 gene cac. The authors generate a series of cac alleles in which one or the other mutually exclusive exons are deleted to determine the functional consequences at the neuromuscular junction. They find alternative splicing at one exon encoding part of the voltage sensor impacts the activation voltage as well as localization to the active zone. In contrast, splicing at the second exon pair does not impact Cav2 channel localization, but it appears to determine the abundance of the channel at active zones. Together, the authors propose that alternative splicing at the Cac locus enables diversity in Cav2 function generated through isoform diversity generated at the single Cav2 alpha subunit gene encoded in Drosophila.

Overall this is an excellent, rigorously validated study that defines unanticipated functions for alternative splicing in Cav2 channels. The authors have generated an important toolkit of mutually exclusive Cac splice isoforms that will be of broad utility for the field, and show convincing evidence for distinct consequences of alternative splicing of this single Cav2 channel at synapses. Importantly, the authors use electrophysiology and quantitative live sptPALM imaging to determine the impacts of Cac alternative splicing on synaptic function. There are some outstanding questions regarding the mechanisms underlying the changes in Cac localization and function, and some additional suggestions are listed below for the authors to consider in strengthening this study. Nonetheless, this is a compelling investigation of alternative splicing in Cav2 channels that should be of interest to many researchers.

eLife assessment

This is an important study that describes an elegant modelling driven approach to design of allosteric antagonists for CXCR4 that have a selective effect on receptor nanocluster formation, cell polarisation and chemotaxis, but spare binding of CXCL12 to the receptor and inhibition of adenylate cyclase. This enables selective targeting of processes dependent upon cell polarisation and chemotaxis without impacting signalling effects and may avoid some of the toxicity associated with antagonists that target CXCL12 binding and thus block all CXCR4 signalling. The revised manuscript offers convincing evidence to support the claims. The modelling work is better described and additional data has been presented that better illustrates the unique features of the new antagonist. The in vivo studies in the zebrafish model open a path to studies in mammalian models.

Reviewer #2 (Public Review):

Summary:

This work describes a new pharmacological targeting approach to inhibit selective functions of the ubiquitously expressed chemokine receptor CXCR4, a potential target of immunomodulatory or anti-cancer treatments. Overall, the results build a strong case for the potential of this new compound to target specific functions of CXCR4, particularly linked to tumorigenesis. However, a more thorough evaluation of the function of the compound as well as future studies in mammalian model systems are needed to better assess the promise of the compound.

Strengths:

The work elegantly utilizes in silico drug modelling to propose new small molecule compounds with specific features. This way, the authors designed compound AGR1.137, which abolishes ligand-induced CXCR4 receptor nanoclustering and the subsequent directed cell migration without affecting ligand-binding itself or some other ligand-induced signaling pathways. The authors have used a relatively broad set of experiments to validate and demonstrate the effects of the drug. Importantly, the authors also test AGR1.137 in vivo, using a zebra fish model of tumorigenesis and metastasis. A relatively strong inhibitory effect of the compound is reported.

Weaknesses:

The authors have been able to significantly strengthen their data from the first submission. The content of this manuscript is pretty solid, although studies in mammalian model systems are naturally needed in the future to better assess the promise of the compound.

Author response:

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

Reviewer #1

(1) In the "Introduction" section, an important aspect that requires attention pertains to the discussion surrounding the heterodimerization of CXCR4 and CCR5. Notably, the manuscript overlooks a recent study (https://doi.org/10.1038/s41467-023-42082-z) elucidating the mechanism underlying the formation of functional dimers within these G protein-coupled receptors (GPCRs)…The inclusion of this study within the manuscript would significantly enrich the contextual framework of the work, offering readers a comprehensive understanding of the current knowledge surrounding the structural dynamics and functional implications of CXCR4 and CCR5 heterodimerization.

We thank the reviewer for his/her recommendation to enrich the contextual framework of our study. The Nature Communications paper by Di Marino et al. was published after we sent the first version of our manuscript to eLife, and therefore was not included in the discussion. As the reviewer rightly indicates, this paper elucidates the mechanism underlying the formation of functional dimers within CCR5 and CXCR4. Using metadynamics approaches, the authors emphasize the importance of distinct transmembrane regions for dimerization of the two receptors. In particular, CXCR4 shows two low energy dimer structures and the TMVI-TMVII helices are the preferred interfaces involved in the protomer interactions in both cases. Although the study uses in silico techniques, it also includes the molecular binding mechanism of CCR5 and CXCR4 in the membrane environment, as the authors generate a model in which the receptors are immersed in a 1-palmitoyl-2-oleoyl-sn-glycero-3-phosphocholine (POPC) phospholipid bilayer with 10% cholesterol. This is an important point in this study, as membrane lipids also interact with membrane proteins, and the lipid composition affects CXCR4 oligomerization (Gardeta S.R. et al. Front. Immunol. 2023). In particular, Di Marino et al. find a cholesterol molecule placed in-between the two CXCR4 protomers where it engages a series of hydrophobic interactions with residues including Leu132, Val214, Leu216 and Phe249. Then, the polar head of cholesterol forms an H-bond with Tyr135 that further stabilizes protomer binding. In our hands, the F249L mutation in CXCR4 reverted the antagonism of AGR1.137, suggesting that the compound binds, among others, this residue. We should, nonetheless, indicate that we analyzed receptor oligomerization and not CXCR4 dimerization, which was the main object of the Di Marino et al. study. It is therefore also plausible that other residues than those described as essential for CXCR4 dimerization might participate in receptor oligomerization. We can speculate that AGR1.137 might affect cholesterol binding to CXCR4 and, therefore, alter dimerization/oligomerization. Additionally, the CXCR4 x-ray structure with PDB code 3ODU (Wu B. et al. Science, 2010) experimentally shows the presence of two fatty acid molecules in contact with both TMV and TMVI. These molecules closely interact with hydrophobic residues in the protein, thereby stabilizing it in a hydrophobic environment. Although more experiments will be needed to clarify the mechanism involved, our results suggest that cholesterol and/or other lipids also play an important role in CXCR4 oligomerization and function, as seen for other GPCRs (Jakubik J. & ElFakahani E.E. Int J Mol Sci. 2021). However, we should also consider that other factors not included in the analysis by Di Marino et al. can also affect CXCR4 oligomerization; for instance, the co-expression of other chemokine receptors and/or other GPCRs that heterodimerize with CXCR4 might affect CXCR4 dynamics at the cell membrane, similar to other membrane proteins such as CD4, which also forms complexes with CXCR4 (Martinez-Muñoz L. et al. Mol. Cell 2018).

The revised discussion contains references to the study by Di Marino et al. to enrich the contextual framework of our data.

(2) In "various sections" of the manuscript, there appears to be confusion surrounding the terminology used to refer to antagonists. It is recommended to provide a clearer distinction between allosteric and orthosteric antagonists to enhance reader comprehension. An orthosteric antagonist typically binds to the same site as the endogenous ligand, directly blocking its interaction with the receptor. On the other hand, an allosteric antagonist binds to a site distinct from the orthosteric site, inducing a conformational change in the receptor that inhibits the binding of the endogenous ligand. By explicitly defining the terms "allosteric antagonist" and "orthosteric antagonist" within the manuscript, readers will be better equipped to discern the specific mechanisms discussed in the context of the study.

The behavior of the compounds described in our manuscript (AGR1.35 and AGR1.137) fits with the definition of allosteric antagonists, as they bind on a site distinct from the orthosteric site, although they only block some ligand-mediated functions and not others. This would mean that they are not formally antagonists and should be not considered as allosteric compounds, as their binding on CXCR4 does not alter CXCL12 binding, although they might affect its affinity. In this sense, our compounds respond much better to the concept of negative allosteric modulators (Gao Z.-G. & Jacobson K.A. Drug Discov. Today Technol. 2013). They act by binding on a site distinct from the orthosteric site and selectively block some downstream signaling pathways but not others induced by the same endogenous agonist.

To avoid confusion and to clarify the role of the compounds described in this study, we now refer to them as negative allosteric modulators along the manuscript.

(3) In the Results section, the computational approach employed for "screening small compounds targeting CXCR4, particularly focusing on the inhibition of CXCL12-induced CXCR4 nanoclustering", requires clarification due to several points of incomprehension. The following recommendations aim to address these concerns and enhance the overall clarity of the section:

(1) Computational Approach and Binding Mode Description: 

-Explicitly describe the methodology for identifying the pocket/clef area in angstroms (Å) on the CXCR4 protein structure. Include details on how the volume of the cleft enclosed by TMV and TMVI was determined, as this information is not readily apparent in the provided reference (https://doi.org/10.1073/pnas.1601278113).

The identification of the cleft was based on the observations by Wu et al. (Wu B. et al. Science 2010) who described the presence of bound lipids in the area formed by TMV and VI, and those of Wescott et al. (Wescott M.P. et al. Proc. Natl. Acad. Sci. 2016) on the importance of TMVI in the transmission of conformational changes promoted by CXCL12 on CXCR4 towards the cytoplasmic surface of the receptor to link the binding site with signaling activation. Collectively, these results, and our previous data on the critical role of the N-terminus region of TMVI for CXCR4 oligomerization (Martinez-Muñoz L. et al. Mol. Cell 2018), focused our in silico screening to this region. Once we detected that several compounds bound CXCR4 in this region, the cleavage properties were calculated by subtracting the compound structure. The resulting PDB was analyzed using the PDBsum server (Laskowski R.A. et. al. Protein Sci. 2018). Volume calculations were obtained using the server analyzing surface clefts by SURFNET (Laskowski R. A. J. Mol. Graph. 1995). The theoretical interaction surface between the selected compounds and CXCR4 and the atomic distances between the protein residues and the compounds was calculated using the PISA server (Krissinel E. & Henrick K. J. Mol. Biol. 2007) (Fig. I, only for review purposes). The analysis of the cleft occupied by AGR1.135 showed two independent cavities of 434 Å3 and 1,381 Å3 that were not connected to the orthosteric site. In the case of AGR1.137, the data revealed two distinct clefts of 790 Å3 and 580 Å3 (Fig. I, only for review purposes). These details have been included in the revised manuscript (New Fig. 1A, Supplementary Fig 8A, B).

(4) Clarify the statement regarding the cleft being "surface exposed for interactions with the plasma membrane," particularly in the context of its embedding within the membrane.

For GPCRs, transmembrane domains represent binding sites for bioactive lipids that play important functional and physiological roles (Huwiler A. & Zangemeister-Wittke U. Pharmacol. Ther. 2018). The channel between TMV and TMVI connects the orthosteric chemokine binding pocket to the lipid bilayer and is occupied by an oleic acid molecule, according to the CXCR4 structure published in 2010 (Wu B. et al. Science 2010). In addition, the target region contains residues involved in cholesterol (and perhaps other lipids) engagement (Di Marino et al. Nat. Commun. 2023). Taken together, these data support our statement that the cleft supports interactions between CXCR4 molecules and the plasma membrane. 

Moreover, the data of Di Marino et al. also support that CCR5 and CXCR4 have a symmetric and an asymmetric binding mode. Therefore, either dimeric structure has the possibility to form trimers, tetramers, and even oligomers by using the free binding interface to complex with another protomer. This hypothesis suggests that the interaction of dimers to form oligomers should involve residues distinct from those included in the dimeric conformation.

The sentence has been modified in the revised manuscript to clarify comprehension.

(5) Discuss the rationale behind targeting the allosteric binding pocket instead of the orthosteric pocket, outlining potential advantages and disadvantages.

The advantages and disadvantages of using negative allosteric modulators vs orthosteric antagonists have been now included in the revised discussion. 

The majority of GPCR-targeted drugs function by binding to the orthosteric site of the receptor, and are agonists, partial agonists, antagonists or inverse agonists. These orthosteric compounds can have off-target effects and poor selectivity due to highly homologous receptor orthosteric sites and to abrogation of spatial and/or temporal endogenous signaling patterns. 

The alternative is to use allosteric modulators, which can tune the functions associated with the receptors without affecting the orthosteric site. They can be positive, negative or neutral modulators, depending on their effect on the functionality of the receptor (Foster D.J. & Conn P.J. Neuron 2017). For example, the use of a negative allosteric modulator of a chemokine receptor to dampen pathological signaling events, while retaining full signaling for non-pathological activities might limit adverse effects (Kohout T.A.et al. J. Biol. Chem. 2004). In this case, the negative allosteric modulator 873140 blocks CCL3 binding on CCR5 but does not alter CCL5 binding (Watson C. et al. Mol. Pharmacol. 2005). In other cases, allosteric modulators can stabilize a particular receptor conformation and block others. The mechanism of action of the anti-HIV-1, FDAapproved, CCR5 allosteric modulator, maraviroc (Jin J. et al. Sci. Signal. 2018) is attributed to its ability to modulate CCR5 dimer populations and their subsequent subcellular trafficking and localization to the cell membrane (Jin J .et al. Sci. Signal. 2018). Two CCR5 dimeric conformations that are imperative for membrane localization were present in the absence of maraviroc; however, an additional CCR5 dimer conformation was discovered after the addition of maraviroc, and all homodimeric conformations were further stabilized. This finding is consistent with the observation that CCR5 dimers and oligomers inhibit HIV host-cell entry, likely by preventing the HIV-1 co-receptor formation.

It is well known that GPCRs activate G proteins, but they also recruit additional proteins (e.g., β-arrestins) that induce signaling cascades which, in turn, can direct specific subsets of cellular responses independent of G protein activation (Eichel K. et al. Nature 2018) and are responsible for either therapeutic or adverse effects. Allosteric modulators can thus be used to block these adverse effects without influencing the therapeutic benefits. This was the case in the design of G protein-biased agonists for the kappa opioid receptor, which maintain the desirable antinociceptive and antipruritic effects and eliminate the sedative and dissociative effects in rodent models (Brust T.F. et al. Sci. Signal 2016).

(6) Provide the PDB ID of the CXCR4 structure used as a template for modeling with SwissModel. Explain the decision to model the structure from the amino acid sequence and suggest an alternative approach, such as utilizing AlphaFold structures and performing classical molecular dynamics with subsequent clustering for the best representative structure.

The PDB used as a template for modeling CXCR4 was 3ODU. This information was already included in the material and methods section. At the time we performed these analyses, there were several crystallographic structures of CXCR4 in complex with different molecules and peptides deposited at the PDB. None of them included a full construct containing the complete receptor sequence to provide a suitable sample for Xray structure resolution, as the N- and C-terminal ends of CXCR4 are very flexible loops. In addition, the CXCR4 constructs contained T4 lysozyme inserted between helices TMV and TMVI to increase the stability of the protein––a common strategy used to facilitate crystallogenesis of GPCRs (Zou Y. et al. PLoS One 2012). Therefore, we generated a CXCR4 homology model using the SWISS-MODEL server (Waterhouse A. et al. Nucleic Acids Res. 2018). This program reconstructed the loop between TMV and TMVI, a domain particularly important in this study that was not present in any of the crystal structure available in PDB. The model structure was, nonetheless, still incomplete, as it began at P27 and ended at S319 because the terminal ends were not resolved in the crystal structure used as a template. Nevertheless, we considered that these terminal ends were not involved in CXCR4 oligomerization. 

As Alphafold was not available at the time we initiated this project, we didn’t use it. However, we have now updated our workflow to current methods and predicted the structure of the target using AlphaFold (Jumper J. et al. Nature 2021) and the sequence available under UniProt entry P61073. We prepared the ligands using OpenBabel (O’Boyle N.M. et al., J. Cheminformatics 2011), with a gasteiger charge assignment, and generated 10 conformers for each input ligand using the OpenBabel genetic algorithm. We then prepared the target structure with Openmm, removing all waters and possible heteroatoms, and adding all missing atoms. We next predicted the target binding pockets with fPocket (Le Guilloux V. et al. BMC Bioinformatics 2009), p2rank (Krivak R. & Hoksza, J. Cheminformatics 2018), and AutoDock autosite (Ravindranath P.A. & Sanner M.F. Bioinformatics 2016). We chose only those pockets between TMV and TMVI (see answer to point 3). We merged the results of the three programs into so-called consensus pockets, as two pockets are said to be sufficiently similar if at least 75% of their surfaces are shared (del Hoyo D. et al. J. Chem. Inform. Model. 2023). From the consensus pockets, there was one pocket that was significantly larger than the others and was therefore selected. We then docked the ligand conformers in this pocket using AutoDock GPU (Santos-Martins D. et al. J. Chem. Theory Comput. 2021), LeDock (Liu N & Xu Z., IOP Conf. Ser. Earth Environ. Sci. 2019), and Vina (Eberhardt J. et al. J. Chem. Inf. Model. 2021). The number of dockings varied from 210 to 287 poses. We scored each pose with the Vina score using ODDT (Wójcikowski M. et al. J. Cheminform. 2015). Then, we clustered the different solutions into groups whose maximum RMSD was 1Å. This resulted in 40 clusters, the representative of each cluster was the one with maximum Vina score and confirmed that the selected compounds bound this pocket (Author response image 1). When required, we calculated the binding affinity using Schrodinger’s MM-GBSA procedure (Greenidge P.A. et al. J. Chem. Inf. Model. 2013), in two ways: first, assuming that the ligand and target are fixed; second, with an energy minimization of all the atoms within a distance of 3Å from the ligand. This information has now been included in the revised version of the manuscript.

Author response image 1.

AGR1.135 docking in CXCR4 using the updated protocol for ligand docking. Cartoon representation colored in gray with TMV and TMVI shown in blue and pink, respectively. AGR1.135 is shown in stick representation with carbons in yellow, oxygens in red and nitrogens in blue.

(7) Specify the meaning of "minimal interaction energy" and where (if present) the interaction scores are reported in the text.

We refer to minimal interaction energy, the best docking score, that is, the best score obtained in our docking studies. These data were not included in the previous manuscript due to space restrictions but are now included in the reviewed manuscript.

(8) You performed docking studies using GLIDE to identify potential binding sites for the small compounds on the CXCR4 protein. The top-scoring binders were then subjected to further refinement using PELE simulations. However, I realize that a detailed description of the specific binding modes of these compounds was not provided in the text. Please make the description of binding poses more detailed

Firstly, to assess the reliability of this method, a PELE study was carried out for the control molecule IT1t, which is a small drug-like isothiourea derivative that has been crystallized in complex with CXCR4 (PDB code: 3ODU). IT1t is a CXCR4 antagonist that binds to the CXCL12 binding cavity and inhibits HIV-1 infection (Das D. Antimicrob. Agents Chemother. 2015; Dekkers S. et al. J. Med. Chem. 2023). From the best five trajectories, two of them had clearly better binding energies, and corresponded to almost the same predicted pose of the molecule. Although the predicted binding mode was not exactly the same as the one in the crystal structure, the approximation was very good, giving validation to the approach. Although PELE is a suitable technique to find potential binding sites, the predicted poses must be subsequently refined using docking programs.

Analyzing the best trajectories for the remaining ligands, at least one of the best-scored poses was always located at the orthosteric binding site of CXCR4. Even though these poses showed good binding energies, they were discarded as the in vitro biological experiments indicated that the compounds were unable to block CXCL12 binding or CXCL12-mediated inhibition of cAMP release or CXCR4 internalization. Collectively, these data indicated that the selected compounds did not behave as orthosteric inhibitors of CXCR4. The CXCL12 binding pocket is the biggest cavity in CXCR4, and so PELE may tend to place the molecules near it. However, all the compounds presented other feasible binding sites with a comparable binding energy.

AGR1.135 and AGR1.137 showed interesting poses between TMV and TMVI with very good binding energy (-51.4 and -37.2 kcal/mol, respectively). This was precisely the region we had previously selected for the in silico screening, as previously described (see response to point 3).

AGR1.131 showed two poses with low binding energy that were placed between helices TMI and TMVII (-43.6 kcal/mol) and between helices TMV and TMVI (-39.8 kcal/mol). This compound was unable to affect CXCL12-mediated chemotaxis and was therefore used as an internal negative control as it was selected in the in silico screening with the same criteria as the other compounds but failed to alter any CXCL12-mediated functions. PELE studies nonetheless provided different binding sites for each molecule, which had to be further studied using docking to obtain a more accurate binding mode. In agreement with the previous commentary, we repeated the analysis using AlphaFold and the rest of the procedure described (see our response to point 6) and calculated the binding energies for all the compounds using Schrodinger’s MM-GBSA procedure (Greenidge P.A. et al. J. Chem. Inf. Model. 2013). Calculations were performed in two ways: first, assuming that the ligand and target are fixed; second, with an energy minimization of all the atoms within a distance of 3Å from the ligand. The results using the first method indicated that AGR1.135 and AGR1.137 showed poses between TMV and TMVI with - 56.4 and -62.4 kcal/mol, respectively and AGR1.131 had a pose between TMI and TMVII with -61.6kcal/mol.  In the second method AGR1.135 and AGR1.137 showed poses between TMV and TMVI with -57.9, and -67.6 kcal/mol, respectively, and AGR1.131 of -62.2 kcal/mol between TMI and TMVII.

This information is now included in the text.

(9) (2) Experimental Design:-Justify the choice of treating Jurkat cells with a concentration of 50 μM of the selected compound. Consider exploring different concentrations and provide a rationale for the selected dosage. Additionally, clearly identify the type of small compound used in the initial experiment.

The revised version contains a new panel in Fig. 1B to show a more detailed kinetic analysis with different concentrations (1-100 µM) of the compounds in the Jurkat migration experiments. In all cases, 100 µM nearly completely abrogated cell migration, but in order to reduce the amount of DMSO added to the cells we selected 50 µM for further experiments, as it was the concentration that inhibits 50-75% of ligand-induced cell migration. Regarding the type of small compounds used in the initial experiments, they were compounds included in the library described in reference #24 (Sebastian-Pérez V. et al Med. Biol. Chem. 2017), which contains heterocyclic compounds. We would note that we do not consider AGR1.137 a final compound. We think that there is scope to develop AGR1.137-based second-generation compounds with greater solubility in water, greater specificity or affinity for CXCR4, and to evaluate delivery methods to hopefully increase activity.  

(10) Avoid reporting details in rounded parentheses within the text; consider relocating such information to the Materials and Methods section or figure captions for improved readability.

Most of the rounded parentheses within the text have been eliminated in the revised version of the manuscript to improve readability.

(11) Elaborate on the virtual screening approach using GLIDE software, specifying the targeted site and methodology employed.

For the virtual screening, we used the Glide module (SP and XP function scoring) included in the Schrödinger software package, utilizing the corresponding 3D target structure and our MBC library (Sebastián-Pérez V et al. J. Chem. Inf. Model. 2017).  The center of the catalytic pocket was selected as the centroid of the grid. In the grid generation, a scaling factor of 1.0 in van der Waals radius scaling and a partial charge cutoff of 0.25 were used. A rescoring of the SP poses of each compound was then performed with the XP scoring function of the Glide. The XP mode in Glide was used in the virtual screening, the ligand sampling was flexible, epik state penalties were added and an energy window of 2.5 kcal/mol was used for ring sampling. In the energy minimization step, the distance-dependent dielectric constant was 4.0 with a maximum number of minimization steps of 100,000. In the clustering, poses were considered as duplicates and discarded if both RMS deviation is less than 0.5 Å and maximum atomic displacement is less than 1.3 Å.

(12) Provide clarity on the statement that AGR1.131 "theoretically" binds the same motif, explaining the docking procedure used for this determination.

In the in silico screening, AGR1.131 was one of the 40 selected compounds that showed, according to the PELE analysis (see answer to point 8), a pose with low binding energy (-39.8 kcal/mol) between TMV and TMVI helices, which is the selected area for the screening. It, nonetheless, also showed a best pose placed between helices TM1 and TM7 (-43.7 kcal/mol) using the initial workflow. In conclusion, although AGR1.131 also faced to the TMV-TMVI, the most favorable pose was in the area between TMI and TMVII. In addition, the compound was included in the biological screening, where it did not affect CXCL12-mediated chemotaxis. We thus decided to use it as an internal negative control, as it has a skeleton very similar to AGR1.135 and AGR1.137 and can interact with the TM domains of CXCR4 without promoting biological effects. This statement has been clarified in the revised text.

(13) Toxicity Testing:

-Enhance the explanation of the approach to testing the toxicity of the compound in Jurkat cells. Consider incorporating positive controls to strengthen the assessment and clarify the experimental design.

All the selected compounds in the in silico screening were initially tested for propidium iodide incorporation in treated cells in a toxicity assay, and some of them were discarded for further experiments (e.g., AGR1.103 and VSP3.1).

Further evaluation of Jurkat cell viability was determined by cell cycle analysis using propidium iodide.  Supplementary Fig. 1B included the percentage of each cell cycle phase, and data indicated no significant differences between the treatments tested. Nevertheless, at the suggestion of the reviewer, and to clarify this issue, positive controls inducing Jurkat cell death (staurosporine and hydrogen peroxide) have also been included in the new Supplementary Fig. 2. The new figure also includes a table showing the percentage of cells in each cell-cycle phase.  

(14) In the Results section concerning "AGR1.135 and AGR1.137 blocking CXCL12-mediated CXCR4 nanoclustering and dynamics", several points can be improved to enhance clarity and coherence: 1. Specificity of Low Molecular Weight Compounds:  

-Clearly articulate how AGR1.135 and AGR1.137 specifically target homodimeric CXCR4 and provide an explanation for their lack of impact on heterodimeric CXCR4-CCR5 in that region.

First of all, we should clarify that when we talk about receptor nanoclustering, oligomers refer to complexes including 3 or more receptors and, therefore, the residues involved in these interactions can differ from those involved in receptor dimerization. Moreover, our FRET experiments did not indicate that the compounds alter receptor dimerization (see new Supplementary Fig. 7). Of note, mutant receptors unable to oligomerize can still form dimers (Martínez-Muñoz L. et al. Mol. Cell 2018; García-Cuesta E.M .et al. Proc. Natl. Acad. Sci. USA 2022). Additionally, we believe that these oligomers can also include other chemokine receptors/proteins expressed at the cell membrane, which we are currently studying using different models and techniques.

We have results supporting the existence of CCR5/CXCR4 heterodimers (Martínez-Muñoz L et al. Proc. Natl. Acad. Sci. USA 2014), in line with the data published by Di Marino et al. However, in the current study we have not evaluated the impact of the selected compounds on other CXCR4 complexes distinct from CXCR4 oligomers. Our Jurkat cells do not express CCR5 and, therefore, we cannot discuss whether AGR1.137 affects CCR5/CXCR4 heterodimers. The chemokine field is very complex and most receptors can form dimers (homo- and heterodimers) as well as oligomers (Martinez-Muñoz L., et al Pharmacol & Therap. 2011) when co-expressed. To evaluate different receptor combinations in the same experiment is a complex task, as the number of potential combinations between distinct expressed receptors makes the analysis very difficult. We started with CXCR4 as a model, to continue later with other possible CXCR4 complexes. In addition, for the analysis of CCR5/CXCR4 dynamics, it is much better to use dual-TIRF techniques, which allow the simultaneous detection of two distinct molecules coupled to different fluorochromes.

Regarding the data of Di Marino et al., it is possible that the compounds might also affect heterodimeric conformations of CXCR4. This aspect has also been broached in the revised discussion. We would again note that we evaluated CXCR4 oligomers and not monomers or dimers; this is especially relevant when we compare the residues involved in these processes as they might differ depending on the receptor conformation considered. This issue was also hypothesized by Di Marino et al. (see our response to point 4).

(15) When referring to "unstimulated" cells, provide a more detailed explanation to elucidate the experimental conditions and cellular state under consideration.

Unstimulated cells refer to the cells in basal conditions, that is, cells in the absence of CXCL12. For TIRF-M experiments, transiently-transfected Jurkat cells were plated on glass-bottomed microwell dishes coated with fibronectin; these are the unstimulated cells. To observe the effect of the ligand, dishes were coated as above plus CXCL12 (stimulated cells). We have clarified this point in the material and methods section of the revised version.

(16) 2. Paragraph Organization

-Reorganize the second paragraph to eliminate redundancy and improve overall flow. A more concise and fluid presentation will facilitate reader comprehension and engagement.

The second paragraph has been reorganized to improve overall flow.

(17) Ensure that each paragraph contributes distinct information, avoiding repetition and redundancy.

We have carefully revised each paragraph of the manuscript to avoid redundancy.

(18) 3. Claim of Allosteric Antagonism:

-Exercise caution when asserting that "AGR1.135 and AGR1.137 behave as allosteric antagonists of CXCR4" based on the presented results. Consider rephrasing to reflect that the observed effects suggest the potential allosteric nature of these compounds, acknowledging the need for further investigations and evidence.

To avoid misinterpretations on the effect of the compounds on CXCR4, as we have commented in our response to point 2, we have substituted the term allosteric inhibitors with negative allosteric modulators, which refer to molecules that act by binding a site distinct from the orthosteric site, and selectively block some downstream signaling pathways, whereas others induced by the same endogenous or orthosteric agonist are unaffected (Gao Z.-G. & Jacobson K.A. Drug Discov. Today Technol. 2013). Our data indicate that the selected small compounds do not block ligand binding or G protein activation or receptor internalization, but inhibit receptor oligomerization and ligand-mediated directed cell migration.

(19) In the Results section discussing the "incomplete abolition of CXCR4-mediated responses in Jurkat cells by AGR1.135 and AGR1.137", several points can be refined for better clarity and completeness:  1. Inclusion of Positive Controls: 

-Consider incorporating positive controls in relevant experiments to provide a comparative benchmark for assessing the impact of AGR1.135 and AGR1.137. This addition will strengthen the interpretation of results and enhance the experimental rigor. 

The in vivo experiments (Fig. 7E,F) used AMD3100, an orthosteric antagonist of CXCR4, as a positive control. We also included AMD3100, as a positive control of inhibition when evaluating the effect of the compounds on CXCL12 binding (Fig. 3, new Supplementary Fig. 3). The revised version of the manuscript also includes the effect of this inhibitor on other relevant CXCL12-mediated responses such as cell migration (Fig. 1B), receptor internalization (Fig. 3A), cAMP production (Fig. 3C), ERK1/2 and AKT phosphorylation (Supplementary Fig. 4), actin polymerization (Fig. 4A), cell polarization (Fig. 4B, C) and cell adhesion (Fig. 4D), to facilitate the interpretation of the results and improve the experimental rigor.

(20) 2. Clarification of Terminology: 

-Clarify the term "CXCR4 internalizes" by providing context, perhaps explaining the process of receptor internalization and its relevance to the study.

We refer to CXCR4 internalization as a CXCL12-mediated endocytosis process that results in reduction of CXCR4 levels on the cell surface. We use CXCR4 internalization in this study with two purposes: First, for CXCR4 and other chemokine receptors, internalization processes are mediated by ligand-induced clathrin vesicles (Venkatesan et al 2003) a process that triggers CXCR4 aggregation in these vesicles. We have previously determined that the oligomers of receptors detected by TIRF-M remain unaltered in cells treated with inhibitors of clathrin vesicle formation and of internalization processes (Martinez-Muñoz L. et al. Mol. Cell 2018). Moreover, we have described a mutant CXCR4 that cannot form oligomers but internalizes normally in response to CXCL12 (Martinez-Muñoz L. et al. Mol. Cell 2018). The observation in this manuscript of normal CXCL12-mediated endocytosis in the presence of the negative allosteric inhibitors of CXCR4 that abrogate receptor oligomerization reinforces the idea that the oligomers detected by TIRF are not related to receptor aggregates involved in endocytosis; Second, receptor internalization is not affected by the allosteric compounds, indicating that they downregulate some CXCL12-mediated signaling events but not others (new Fig. 3).

All these data have been included in the revised discussion of the manuscript.

(21) Elaborate on the meaning of "CXCL12 triggers normal CXCR4mut internalization" to enhance reader understanding.

We have previously described a triple-mutant CXCR4 (K239L/V242A/L246A; CXCR4mut). The mutant residues are located in the N-terminal region of TMVI, close to the cytoplasmic region, thus limiting the CXCR4 pocket described in this study (see our response to point 3). This mutant receptor dimerizes but neither oligomerizes in response to CXCL12 nor supports CXCL12-induced directed cell migration, although it can still trigger some Ca2+ flux and is internalized after ligand activation (Martinez-Muñoz L. et al. Mol. Cell 2018).  We use the behavior of this mutant (CXCR4mut) to show that the CXCR4 oligomers and the complexes involved in internalization processes are not the same and to explain why we evaluated CXCR4 endocytosis in the presence of the negative allosteric modulators.

As we indicated in a previous answer to the reviewer, these issues have been re-elaborated in the revised version.

(22) 3. Discrepancy in CXCL12 Concentration:

-Address the apparent discrepancy between the text stating, "...were stimulated with CXCL12 (50 nM, 37{degree sign}C)," and the figure caption (Fig. 3A) reporting a concentration of 12.5 nM. Rectify this inconsistency and provide an accurate and clear explanation.

We apologize for this error, which is now corrected in the revised manuscript. With the exception of the cell migration assays in Transwells, where the optimal concentration was established at 12.5 nM, in the remaining experiments the optimal concentration of CXCL12 employed was 50 nM. These concentrations were optimized in previous works of our laboratory using the same type of experiment. We should also remark that in the experiments using lipid bilayers or TIRF-M experiments, CXCL12 is used to coat the plates and therefore it is difficult to determine the real concentration of the ligand that is retained in the surface of the plates after the washing steps performed prior to adding the cells. In addition, we use 100 nM CXCL12 to create the gradient in the chambers used to perform the directed-cell migration experiments.

(23) 4. Speculation on CXCL12 Binding:

-Refrain from making speculative statements, such as "These data suggest that none of the antagonists alters CXCL12 binding to CXCR4," unless there is concrete evidence presented up to that point. Clearly outline the results that support this conclusion.

Figure 3B and Supplementary Figure 3 show CXCL12-ATTO700 binding by flow cytometry in cells pretreated with the negative allosteric modulators. We have also included AMD3100, the orthosteric antagonist, as a control for inhibition. While these experiments showed no major effect of the compounds on CXCL12 binding, we cannot discard small changes in the affinity of the interaction between CXCL12 and CXCR4. In consequence we have re-written these statements.

(24) 5. Corroboration of Data:

-Specify where the corroborating data from immunostaining and confocal analysis are reported, ensuring readers can access the relevant information to support the conclusions drawn in this section.

In agreement with the suggestion of the reviewer, the revised manuscript includes data from immunostaining and confocal analysis to complement Fig. 4B (new Fig. 4C). The revised version also includes some representative videos for the TIRF experiments showed in Figure 2 to clarify readability.

(25) In the Results section concerning "AGR1.135 and AGR1.137 antagonists and their direct binding to CXCR4", several aspects need clarification and refinement for a more comprehensive and understandable presentation: 1. Workflow Clarification:

-Clearly articulate the workflow used for assessing the binding of AGR1.135 and AGR1.137 to CXCR4. Address the apparent contradiction between the inability to detect a direct interaction and the utilization of Glide for docking in the TMV-TMVI cleft.

To address the direct interaction of the compounds with CXCR4, we intentionally avoided the modification of the small compounds with different labels, which could affect their properties. We therefore attempted a fluorescence a spectroscopy strategy to formally prove the ability of the small compounds to bind CXCR4, but this failed because the AGR1.135 is yellow in color, which interfered with the determinations. We also tried a FRET strategy (see new Supplementary Fig. 7) and detected a significant increase in FRET efficiency of CXCR4 homodimers when AGR1.135 was evaluated, but again the yellow color interfered with FRET determinations. Moreover, AGR1.137 did not modify FRET efficiency of CXCR4 dimers. Therefore, we were unable to detect the interaction of the compounds with CXCR4.

We elected to develop an indirect strategy; in silico, we evaluated the binding-site using docking and molecular dynamics to predict the most promising CXCR4 binding residues involved in the interaction with the selected compounds. Next, we generated point mutant receptors of the predicted residues and re-evaluated the behavior of the allosteric antagonists in a CXCL12-induced cell migration experiment. Obviously, we first discarded those CXCR4 mutants that were not expressed on the cell membrane as well as those that were not functional when activated with CXCL12. Using this strategy, we eliminated the interference due to the physical properties of the compounds and demonstrated that if the antagonism of a compound is reversed in a particular CXCR4 mutant it is because the mutated residue participates or interferes with the interaction between CXCR4 and the compound, thus assuming (albeit indirectly) that the compound binds CXCR4. 

To select the specific mutations included in the analysis, our strategy was to generate point mutations in residues present in the TMV-TMVI pocket of CXCR4 that were not directly proposed as critical residues involved in chemokine engagement, signal initiation, signal propagation, or G protein-binding, based on the extensive mutational study published by Wescott MP et. al. (Wescott M.P. et. al. Proc. Natl. Acad. Sci. U S A. 2016).

(26) Provide a cohesive explanation of the transition from docking evaluation to MD analysis, ensuring a transparent representation of the methodology.

Based on the aim of this work, the workflow shown in Author response image 2, was proposed to predict the binding mode of the selected molecules. Firstly, a CXCR4 model was generated to reconstruct some unresolved parts of the protein structure; then a binding site search using PELE software was performed to identify the most promising binding sites; subsequently, docking studies were performed to refine the binding mode of the molecules; and finally, molecular dynamics simulations were run to determine the most stable poses and predict the residues that we should mutate to test that the compounds interact with CXCR4. 

Author response image 2.

Workflow followed to determine the binding mode of the  studied compounds.

(27) 2. Choice of Software and Techniques:

-Justify the use of "AMBER14" and the PELE approach, considering  their potential obsolescence.

These experiments were performed five years ago when the project was initiated. As the reviewer indicates, AMBER14 and PELE approaches might perhaps be considered obsolescent. Thus, we have predicted the structure of the target using AlphaFold (Jumper J. et al, Nature 2021) and the sequence available under UniProt entry P61073. The complete analysis performed (see our response to point 4) confirmed that the compounds bound the selected pocket, as we had originally determined using PELE. These new analyses have been incorporated into the revised manuscript.

(28)-Discuss the role of the membrane in the receptor-ligand interac7on. Elaborate on how the lipidic double layer may influence the binding of small compounds to GPCRs embedded in the membrane.

Biological membranes are vital components of living organisms, providing a diffusion barrier that separates cells from the extracellular environment, and compartmentalizing specialized organelles within the cell. In order to maintain the diffusion barrier and to keep it electrochemically sealed, a close interaction of membrane proteins with the lipid bilayer is necessary. It is well known that this is important, as many membrane proteins undergo conformational changes that affect their transmembrane regions and that may regulate their activity, as seen with GPCRs (Daemen F.J. & Bonting S.L., Biophys. Struct. Mech. 1977; Gether U. et al. EMBO J. 1997). The lateral and rotational mobility of membrane lipids supports the sealing function while allowing for the structural rearrangement of membrane proteins, as they can adhere to the surface of integral membrane proteins and flexibly adjust to a changing microenvironment. In the case of the first atomistic structure of CXCR4 (Wu B. et al. Science 2010), it was indicated that for dimers, monomers interact only at the extracellular side of helices V and VI, leaving at least a 4-Å gap between the intracellular regions, which is presumably filled by lipids. In particular, they indicated that the channel between TMV and TMVI that connects the orthosteric chemokine binding pocket to the lipid bilayer is occupied by an oleic acid molecule. Recently, Di Marino et al., analyzing the dimeric structure of CXCR4, found a cholesterol molecule placed in between the two protomers, where it engages a series of hydrophobic interactions with residues located in the area between TMI and TMVI (Leu132, Val214, Leu216, Leu246, and Phe249). The polar head of cholesterol forms an H-bond with Tyr135 that further stabilizes its binding mode. This finding confirms that cholesterol might play an important role in mediating and stabilizing receptor dimerization, as seen in other GPCRs (Pluhackova, K., et al. PLoS Comput. Biol. 2016). In addition, we have previously observed that, independently of the structural changes on CXCR4 triggered by lipids, the local lipid environment also regulates CXCR4 organization, dynamics and function at the cell membrane and modulates chemokine-triggered directed cell migration. Prolonged treatment of T cells with bacterial sphingomyelinase promoted the complete and sustained breakdown of sphingomyelins and the accumulation of the corresponding ceramides, which altered both membrane fluidity and CXCR4 nanoclustering and dynamics. Under these conditions, CXCR4 retained some CXCL12-mediated signaling activity but failed to promote efficient directed cell migration (Gardeta S.R. et al. Front. Immunol. 2022). Collectively, these data demonstrate the key role that lipids play in the stabilization of CXCR4 conformations and in regulating its lateral mobility, influencing their associated functions. These considerations have been included in the revised version of the manuscript. 

(29) 3. Stable Trajectories and Binding Mode Superimposi7on -Specify the criteria for defining "stable trajectories" to enhance reader understanding

There could be several ways to describe the stability of a MD simulation, based on the convergence of energies, distances or ligand-target interactions, among others. In this work, we use the expression “stable trajectories” to refer to simulations in which the ligand trajectory converges and the ligand RMSD does not fluctuate more than 0.25Å. This definition is now included in the revised text.

(30)  Clarify the meaning behind superimposing the two small compounds and ensure that the statement in the figure caption aligns with the information presented in the main text.

We apologize for the error in the previous Fig. 5A and in its legend. The figure was created by superimposing the protein component of the poses for the two compounds, AGR1.135 and AGR1.137, rather than the compounds themselves. As panel 5A was confusing, we have modified all Fig. 5 in the revised manuscript to improve clarity.

(31) 4. Volume Analysis and Distances:

-Provide details on how the volume analysis was computed and how distances were accounted for. Consider adding a figure to illustrate these analyses, aiding reader comprehension.

The cleft search and analysis were performed using the default settings of SURFNET (Laskowski R.A. J. Mol. Graph. 1995) included in the PDBsum server (Laskowski R.A. et. al. Trends Biochem. Sci. 1997). The first run of the input model for CXCR4 3ODU identified a promising cleft of 870 Å3 in the lower half of the region flanked by TMV and TMVI, highlighting this area as a possible small molecule binding site (Fig. I, only for review purposes). Analysis of the cleft occupied by AGR1.135 showed two independent cavities of 434 Å3 and 1381 Å3 that were not connected to the orthosteric site. The same procedure for AGR1.137 revealed two distinct clefts of 790 Å3 and 580 Å3, respectively (Fig. I, only for review purposes). Analysis of the atomic distances between the protein residues and the compounds was performed using the PISA server. Krissinel E. & Henrick K. J. Mol. Biol. 2007). (Please see our response to point 3 and the corresponding figure).

(32) 5. Mutant Selection and Relevance:

-Clarify the rationale behind selecting the CXCR4 mutants used in the study. Consider justifying the choice and exploring the possibility of performing an alanine (ALA) scan for a more comprehensive mutational analysis.  

The selection of the residues to be mutated along the cleft was first based on their presence in the proposed cleft and the direct interaction of the compounds with them, either by hydrogen bonding or by hydrophobic interactions. Secondly, all mutated residues did not belong to any of the critical residues involved in transmitting the signal generated by the interaction of CXCL12 with the receptor. In any case, mutants producing a non-functional CXCR4 at the cell membrane were discarded after FACS analysis and chemotaxis experiments. Finally, the length and nature of the resulting mutations were designed mainly to occlude the cleft in case of the introduction of long residues such as lysines (I204K, L208K) or to alter hydrophobic interactions by changing the carbon side chain composition of the residues in the cleft. Indeed, we agree that the alanine scan mutation analysis would have been an alternative strategy to evaluate the residues involved in the interactions of the compounds. 

(33) Reevaluate the statement regarding the relevance of the Y256F muta7on for the binding of AGR1.137. If there is a significant impact on migra7on in the mutant (Fig. 6B), elaborate on the significance in the context of AGR1.137 binding.

In the revised discussion we provide more detail on the relevance of Y256F mutation for the binding of AGR1.137 as well as for the partial effect of G207I and R235L mutations. The predicted interactions for each compound are depicted in new Fig. 6 C, D after LigPlot+ analysis (Laskowski R.A. & Swindells M.B. J. Chem. Inf. Model. 2011), showing that AGR1.135 interacted directly with the receptor through a hydrogen bond with Y256. When this residue was mutated to F, one of the anchor points for the compound was lost, weakening the potential interaction in the region of the upper anchor point.

It is not clear how the Y256F mutation will affect the binding of AGR1.137, but other potential contacts cannot be ruled out since that portion of the compound is identical in both AGR1.135 and AGR1.137. This is especially true for its neighboring residues in the alpha helix, F249, L208, as shown in 3ODU structure (Fig. 6D), which are shown to be directly implicated in the interaction of both compounds. Alternatively, we cannot discard that Y256 interacts with other TMs or lipids stabilizing the overall structure, which could reverse the effect of the mutant at a later stage (Author response image 3).

Author response image 3.

Cartoon representation of Y256 and its intramolecular interactions in the CXCR4 Xray solved structure 3ODU. TMV helix is colored in blue and TMVI in pink.

(34) Address the apparent discrepancy in residue involvement between AGR1.135 and AGR1.137, particularly if they share the same binding mode in the same clef.

AGR1.135 and AGR1.137 exhibit comparable yet distinct binding modes, engaging with CXCR4 within a molecular cavity formed by TMV and TMVI. AGR1.135 binds to CXCR4 through three hydrogen bonds, two on the apical side of the compound that interact with residues TMV-G207 and TMVI-Y256 and one on the basal side that interacts with TMVI-R235 (Fig. 5A). This results in a more extended and rigid conformation when sharing hydrogen bonds, with both TMs occupying a surface area of 400 Å2 and a length of 20 Å in the cleft between TMV and TMVI (Supplementary Fig. 8A). AGR1.137 exhibits a distinct binding profile, interacting with a more internal region of the receptor. This interaction involves the formation of a hydrogen bond with TMIIIV124, which induces a conformational shift in the TMVI helix towards an active conformation (Fig. 5B; Supplementary Fig. 13). Moreover, AGR1.137 may utilize the carboxyl group of V124 in TMIII and overlap with AGR1.135 binding in the cavity, interacting with the other 19 residues dispersed between TMV and VI to create an interaction surface of 370 Å2 along 20 Å (Supplementary Fig. 8B). This is illustrated in the new Fig. 5B. AGR1.137 lacks the phenyl ring present in AGR1.135, resulting in a shorter compound with greater difficulty in reaching the lower part of TMVI where R235 sits. 

Author response image 4.

AGR1.135 and AGR1.137 interaction with TMV and TMVI.  The model shows the location of the compounds within the TMV-VI cleft, illustrated by a ribbon and stick representation. The CXCR4 segments of TMV and TMVI are represented in blue and pink ribbons respectively, and side chains for some of the residues defining the cavity are shown in sticks. AGR1.135 and AGR1.137 are shown in stick representation with carbon in yellow, nitrogen in blue, oxygen in red, and fluorine in green. Hydrogen bonds are indicated by dashed black lines, while hydrophobic interactions are shown in green. The figure reproduces the panels A, B of Fig. 5 in the revised manuscript.

(35) In the Results sec7on regarding "AGR1.137 treatment in a zebrafish xenograf model", the following points can be refined for clarity and completeness: 1. Cell Line Choice for Zebrafish Xenograft Model:

-Explain the rationale behind the choice of HeLa cells for the zebrafish xenograft model when the previous experiments primarily focused on Jurkat cells. Address any specific biological or experimental considerations that influenced this decision.

As far as we know, there are no available models of tumors in zebrafish using Jurkat cells. We looked for a tumoral cell system that expresses CXCR4 and could be transplanted into zebrafish. HeLa cells are derived from a human cervical tumor, express a functional CXCR4, and have been previously used for tumorigenesis analyses in zebrafish (Brown H.K. et al. Expert Opin. Drug Discover. 2017; You Y. et al Front. Pharmacol. 2020). These cells grow in the fish and disseminate through the ventral area and can be used to determine primary tumor growth and metastasis. Nonetheless, we first analyzed in vitro the expression of a functional CXCR4 in these cells (Supplementary Fig. 10A), whether AGR1.137 treatment specifically abrogated CXCL12-mediated direct cell migration (Fig. 7A, B), as whether it affected cell proliferation (Supplementary Fig. 10B). As HeLa cells reproduce the in vitro effects detected for the compounds in Jurkat cells, we used this model in zebrafish. These issues were already discussed in the first version of our manuscript. 

(36) 2. Toxicity Assessment in Zebrafish Embryos: 

-Clarify the basis for stating that AGR1.137 is not toxic to zebrafish embryos. Consider referencing the Zebrafish Embryo Acute Toxicity Test (ZFET) and provide relevant data on lethal concentration (LC50) and non-lethal toxic phenotypes such as pericardial edema, head and tail necrosis, malformation, brain hemorrhage, or yolk sac edema.

Tumor growth and metastasis kinetics within the zebrafish model have been extensively evaluated in many publications (White R. et al. Nat. Rev. Cancer. 2013; Astell K.R. and Sieger D. Cold Spring Harb. Perspect. Med. 2020; Chen X. et al. Front. Cell Dev. Biol. 2021; Weiss JM. Et al. eLife 2022; Lindhal G. et al NPJ Precis. Oncol. 2024). Our previous experience using this model shows that tumors start having a more pronounced proliferation and lower degree of apoptosis from day 4 onwards, but we cannot keep the tumor-baring larvae for that long due to ethical reasons and also because we don’t see much scientific benefit of unnecessarily extending the experiments. Anti-proliferative or pro-apoptotic effects of drugs can still be observed within the three days, even if this is then commonly seen as larger reduction (instead of a smaller growth as it is commonly seen in for example mouse tumor models) compared to controls. Initially we characterized the evolution of implanted tumors in our system and how much they metastasize over time in the absence of treatment before to test the compounds (Author response image 5).

The in vivo experiments were planned to validate efficacious concentrations of the investigated drugs rather than to derive in vivo IC50 or other values, which require testing of multiple doses. We have, however, included an additional concentration to show concentration-dependence and therefore on-target specificity of the drugs in the revised version of the manuscript (data also being elaborated in ongoing experiments). At this stage, we believe that adding the LC50 does not provide interesting new knowledge, and it is standard to only show results from the experimental endpoint (in our case 3 days post implantation). We agree that showing these new data points strengthens the manuscript and facilitates independent evaluation and conclusions to be drawn from the presented data. We have created new graphs where datapoints for each compound dose are shown.  

Author response image 5.

Evolution of the tumors and metastasis along the time in the absence of any treatment. HeLa cells were labeled with 8 µg/mL Fast-DiI™ oil and then implanted in the dorsal perivitelline space of 2-days old zebrafish embryos. Tumors were imaged within 2 hours of implantation and re-imaged each 24 h for three days. Changes in tumor size was evaluated as tumor area at day 1, 2 and 3 divided by tumor area at day 0, and metastasis was evaluated as the number of cells disseminated to the caudal hematopoietic plexus at day 1, 2 and 3 divided by the number of cells at day  3.

Regarding the statement that AGR1.137 was not toxic, this was based on visual inspection of the zebrafish larvae at the end of the experiment, which also revealed a lack of drug-related mortality in these experiments. There are a number of differences in how our experiment was run compared with the standardized ZFET. ZFET evaluates toxicity from 0 hours post-fertilization to 1 or 2 days post-fertilization, whereas here we exposed zebrafish from 2 days post-fertilization to 5 days post-fertilization. The ZFET furthermore requires that the embryos are raised at 26ºC whereas kept the temperature as close as possible to a physiologically relevant temperature for the tumor cells (36ºC). In the ZFET, embryos are incubated in 96-well plates whereas for our studies we required larger wells to be able to manipulate the larvae and avoid well edge-related imaging artefacts, and we therefore used 24-well plates. As such, the ZFET was for various reasons not applicable to our experimental settings. As we were not interested in rigorously determining the LD50 or other toxicity-related measurements, as our focus was instead on efficacy and we found that the targeted dose was tolerated, we did not evaluate multiple doses, including lethal doses of the drug, and are therefore not able to determine an LD50/LC50. We also did not find drug-induced non-lethal toxic phenotypes in this study, and so we cannot elaborate further on such phenotypes other than to simply state that the drug is well tolerated at the given doses. Therefore, the reference to ZFET in the manuscript was eliminated.

(37) If supplementary information is available, consider providing it for a comprehensive understanding of toxicity assessments. 

The effective concentration used in the zebrafish study was derived from the in vitro experiments. That being said, and as elaborated in our response to comment 36, we have added data for one additional dose to show the dose-dependent regulation of tumor growth and metastasis. 

(38) 3. Optimization and Development of AGR1.137: 

-Justify the need for further optimization and development of AGR1.137 if it has a comparable effect to AMD3100. Explain the specific advantages or improvements that AGR1.137 may offer over AMD3100. 

AGR1.137 is highly hydrophobic and is very difficult to handle, particularly in in vivo assays; thus, for the negative allosteric modulators to be used clinically, it would be very important to increase their solubility in water. Contrastingly, AMD3100 is a water-soluble compound. Before using the zebrafish model, we performed several experiments in mice using AGR1.137, but the inhibitory results were highly variable, probably due to its hydrophobicity. We also believe that it would be important to increase the affinity of AGR1.137 for CXCR4, as the use of lower concentrations of the negative allosteric modulator would limit potential in vivo side effects of the drug. On the other hand, we are also evaluating distinct administration alternatives, including encapsulation of the compounds in different vehicles. These alternatives may also require modifications of the compounds. 

AMD3100 is an orthosteric inhibitor and therefore blocks all the signaling cascades triggered by CXCL12. For instance, we observed that AMD3100 treatment blocked CXCL12 binding, cAMP inhibition, calcium flux, cell adhesion and cell migration (Fig. 3, Fig. 4), whereas the effects of AGR1.137 were restricted to CXCL12-mediated directed cell migration. Although AMD3100 was well tolerated by healthy volunteers in a singledose study, it also promoted some mild and reversible events, including white blood cells count elevations and variations of urine calcium just beyond the reported normal range (Hendrix C.W. et al. Antimicrob. Agents Chemother. 2000). To treat viral infections, continuous daily dosing requirements of AMD3100 were impractical due to severe side effects including cardiac arrhythmias (De Clercq E. Front Immunol. 2015). For AMD3100 to be used clinically, it would be critical to control the timing of administration. In addition, side effects after long-term administration have potential problems. Shorter-term usage and lower doses would be fundamental keys to its success in clinical use (Liu T.Y. et al. Exp. Hematol. Oncol. 2016). The use of a negative allosteric modulator that block cell migration but do not affect other signaling pathways triggered by CXCL12 would be, at least in theory, more specific and produce less side effects. These ideas have been incorporated into the revised discussion to reflect potential advantages or improvements that AGR1.137 may offer over AMD3100.

(39) 4. Discrepancy in AGR1.137 and AMD3100 Effects:

-Discuss the observed discrepancy where AGR1.137 exhibits similar effects to AMD3100 but only after 48 hours. Provide insights into the temporal dynamics of their actions and potential implications for the experimental design.

Images and data shown in Fig. 7E, F correspond to days 0 and 3 after HeLa cell implantation (tumorigenesis) and only to day 3 in the case of metastasis data. The revised version contains the effect of two distinct doses of the compounds (10 and 50 µM, for AGR1.135 and AGR1.137 and 1 and 10 µM for AMD3100). 

(40) In the "Discussion" section, there are several points that require clarifica7on and refinement to enhance the overall coherence and depth of the analysis:  1. Reduction of Side-Effects: 

-Provide a more detailed explanation of how the identified compounds, specifically AGR1.135 and AGR1.137, contribute to the reduction of side effects. Consider discussing specific mechanisms or characteristics that differentiate these compounds from existing antagonists.

The sentence indicating that AGR1.135 and AGR1.137 contribute to reduce side effects is entirely speculative, as we have no experimental evidence to support it. We have therefore corrected this in the revised version. The origin of the sentence was that orthosteric antagonists typically bind to the same site as the endogenous ligand, thus blocking its interaction with the receptor. Therefore, orthosteric inhibitors (i.e. AMD3100) block all signaling cascades triggered by the ligand and therefore their functional consequences. However, the compounds described in this project are essentially negative allosteric modulators, that is, they bind to a site distinct from the orthosteric site, inducing a conformational change in the receptor that does not alter the binding of the endogenous ligand, and therefore block some specific receptor-associated functions without altering others. We observed that AGR1.137 blocked receptor oligomerization and directed cell migration whereas CXCL12 still bound CXCR4, triggered calcium mobilization, did not inhibit cAMP release or promoted receptor internalization. This is why we speculated on the limitation of side effects. The statements have been nonetheless revised in the new version of the manuscript.

(41) 2. Binding Site Clarification:

-Address the apparent discrepancy between docking the small compounds in a narrow cleft formed by TMV and TMVI helices and the statement that AGR1.131 binds elsewhere. Clarify the rationale behind this assertion

After the in silico screening, a total of 40 compounds were selected.  These compounds showed distinct degrees of interaction with the cleft formed by TMV and TMVI and even with other potential interaction sites on CXCR4, with the exception of the ligand binding site according to the data described by Wescott et al. (PNAS 2016 113:9928-9933), as this possibility was discarded in the initial approach of the in silico screening. According to PELE analysis, AGR1.131 was one of the 40 selected compounds that showed a pose with low binding energy, -39.8 kcal/mol, between TMV and TMVI helices, that is, it might interact with CXCR4 through the selected area for the screening. It nonetheless also showed a best pose placed between helices TMI and TMVII, -43.7 kcal/mol. In any case, the compound was included in the biological screening, where it was unable to impact CXCL12-mediated chemotaxis (Fig. 1B). We then focused on AGR1.135 and AGR1.137, as showed a higher inhibitory effect on CXCL12-mediated migration, and on AGR1.131 as an internal negative control. AGR1.131 has a skeleton very similar to the other compounds (Fig. 1C) and can interact with the TM domains of CXCR4 without promoting effects. None of the three compounds affected CXCL12 binding, or CXCL12mediated inhibition of cAMP release, or receptor internalization. However, whereas AGR1.135 and AGR1.137, blocked CXCL12-mediated CXCR4 oligomerization and directed cell migration towards CXCL12 gradients, AGR1.131 had no effect in these experiments (Fig. 3, Fig.  4). 

Next, we performed additional theoretical calculations (PELE, docking, MD) to inspect in detail the potential binding modes of active and inactive molecules. Based on these additional calculations, we identified that whereas AGR1.135 and AGR1.137 showed preferent binding on the molecular pocket between TMV and TMVI, the best pose for AGR1.131 was located between TMI and TMVII, as the initial experiments indicated.  These observations and data have been clarified in the revised discussion. 

(42) 3. Impact of Chemical Modifications:

-Discuss the consequences of the distinct chemical groups in AGR1.135, AGR1.137, and AGR1.131, specifically addressing how variations in amine length and chemical nature may influence binding affinity and biological activity. Provide insights into the potential effects of these modifications on cellular responses and the observed outcomes in zebrafish. 

The main difference between AGR1.131 and the other two compounds is the higher flexibility of AGR1.131 due to the additional CH2 linker, together with the lack of a piperazine ring. The additional CH2 linking the phenyl ring increases the flexibility of AGR1.131 when compared with AGR1.135 and AGR1.137, and the absence of the piperazine ring might be responsible for its lack of activity, as it makes this compound able to bind to CXCR4 (Fig. 1C).

AGR1.137 was chosen in a second round. The additional presence of the tertiary amine (in the piperazine ring) allows the formation of quaternary ammonium salts in the aqueous medium and its substituents to increase its solubility (Fig 1C). This characteristic might be related to the absence of toxic effects of the compound in the zebrafish model.

(43) 4. Existence of Distinct CXCR4 Conformational States: 

-Provide more detailed support for the statement suggesting the "existence of distinct CXCR4 conformational states" responsible for activating different signaling pathways. Consider referencing relevant studies or experiments that support this claim.

Classical models of GPCR allostery and activation, which describe an equilibrium between a single inactive and a single signaling-competent active conformation, cannot account for the complex pharmacology of these receptors. The emerging view is that GPCRs are highly dynamic proteins, and ligands with varying pharmacological properties differentially modulate the balance between multiple conformations.

Just as a single photograph from one angle cannot capture all aspects of an object in movement, no one biophysical method can visualize all aspects of GPCR activation. In general, there is a tradeoff between high-resolution information on the entire protein versus dynamic information on limited regions. In the former category, crystal and cryo-electron microscopy (cryoEM) structures have provided comprehensive, atomic-resolution snapshots of scores of GPCRs both in inactive and active conformations, revealing conserved conformational changes associated with activation. However, different GPCRs vary considerably in the magnitude and nature of the conformational changes in the orthosteric ligand-binding site following agonist binding (Venkatakrishnan A.J.V. et al. Nature 2016). Spectroscopic and computational approaches provide complementary information, highlighting the role of conformational dynamics in GPCR activation (Latorraca N.R.V. et al. Chem. Rev 2017). In the absence of agonists, the receptor population is typically dominated by conformations closely related to those observed in inactive-state crystal structures (Manglik A. et al. Cell 2015). While agonist binding drives the receptor population towards conformations similar to those in activestate structures, a mixture of inactive and active conformations remains, reflecting “loose” or incomplete allosteric coupling between the orthosteric and transducer pockets (Dror R.O. et al. Proc. Natl. Acad. Sci. USA 2011). Surprisingly, for some GPCRs, and under some experimental conditions, a substantial fraction of unliganded receptors already reside in an active-like conformation, which may be related to their level of basal or constitutive signaling (Staus D.P. et al. J. Biol. Chem. 2019);  Ye L. et al. Nature 2016).  In our case, the negative allosteric modulators, (Staus DP, et al. J. Biol. Chem 2019); Ye L. et al. Nature 2016) did not alter ligand binding and had only minor effects on specific CXCL12-mediated functions such as inhibition of cAMP release or receptor internalization, among others, but failed to regulate CXCL12-mediated actin dynamics and receptor oligomerization. Collectively, these data suggest that the described compounds alter the active conformation of CXCR4 and therefore support the presence of distinct receptor conformations that explain a partial activation of the signaling cascade.

All these observations are now included in the revised discussion of the manuscript.

(44) 5. Equilibrium Shift and Allosteric Ligands: 

-Clarify the statement about "allosteric ligands shifting the equilibrium to favor a particular receptor conformation". Support this suggestion with references or experimental evidence

In a previous answer (see our response to point 2), we explain why we define the compounds as negative allosteric modulators. These compounds do not bind the orthosteric binding site or a site distinct from the orthosteric site that alters the ligand-binding site. Their effect should be due to changes in the active conformation of CXCR4, which allow some signaling events whereas others are blocked. Our functional data thus support that through the same receptor the compounds separate distinct receptor-mediated signaling cascades, that is, our data suggest that CXCR4 has a conformational heterogeneity. It is known that GPCRs exhibit more than one “inactive” and “active” conformation, and the endogenous agonists stabilize a mixture of multiple conformations. Biased ligands or allosteric modulators can achieve their distinctive signaling profiles by modulating this distribution of receptor conformations. (Wingler L.M. & Lefkowitz R.J. Trends Cell Biol. 2020). For instance, some analogs of angiotensin II do not appreciably activate Gq signaling (e.g., increases in IP3 and Ca2+) but still induce receptor phosphorylation, internalization, and mitogen-activated protein kinase (MAPK) signaling (Wei H, et al. Proc. Natl. Acad. Sci. USA 2003). Some of these ligands activate Gi and G12 in bioluminescence resonance energy transfer (BRET) experiments (Namkung Y. et al. Sci. Signal. 2018). A similar observation was described in the case of CCR5, where some chemokine analogs promoted G protein subtype-specific signaling bias (Lorenzen E. et al. Sci. Signal 2018). Structural analysis of distinct GPCRs in the presence of different ligands vary considerably in the magnitude and nature of the conformational changes in the orthosteric ligand-binding site following agonist binding (Venkatakrishnan A.J.V. et al. Nature 2016). Yet, these changes modify conserved motifs in the interior of the receptor core and induce common conformational changes in the intracellular site involved in signal transduction. That is, these modifications might be considered distinct receptor conformations. 

The revised discussion contains some of these interpretations to support our statement about the stabilization of a particular receptor conformation triggered by the negative allosteric modulators. 

(45) 6. Refinement of Binding Mode: 

-Clarify the workflow for obtaining the binding mode, particularly the role of GLIDE and PELE. Clearly explain how these software tools were used in tandem to refine the binding mode. 

The computational sequential workflow applied in this project included, i) Protein model construction, ii) Virtual screening (Glide), iii) PELE, iv) Docking (AutoDock and Glide) and v) Molecular Dynamics (AMBER).

Glide was applied for the structure-based virtual screening to explore which compounds could fit and interact with the previously selected binding site.

After the identification of theoretically active compounds (modulators of CXCR4), additional calculations were done to identify a potential binding site. PELE was used in this sense, to study how the compounds could bind in the whole surface of the target (TMV-TMVI). By applying PELE, we avoided biasing the calculation, and we found that the trajectories with better interaction energies identified the cleft between TMV and TMVI as the binding site for AGR1.135 and AGR1.137, and not for AGR1.131. AGR1.131 showed a pose with low binding energy, -39.8 kcal/mol, between TMV and TMVI helices, that is, it might interact with CXCR4 in the selected area for the screening. But it also showed a better pose placed between helices TMI and TMVII, - 43.7 kcal/mol (see our response to point 41). These data have been now confirmed using Schrodinger’s MM-GBSA procedure (see our response to points 6 and 8). In any case, the compound was included in the biological screening, where it was unable to affect CXCL12-mediated chemotaxis (Fig. 1B). Docking and MD simulations were then performed to study and refine the specific binding mode in this cavity. These data were important to choose the mutations on CXCR4 required, to test whether the compounds reversed its behavior. In these experiments we also confirmed that AGR1.131 had a better pose on the TMI-TMVII region. 

(46) 7. Impact of Compound Differences on CXCR4-F249L mutant: 

-Provide visual aids, such as figures, and additional experiments to support the statement about differences in the behavior of AGR1.135 and AGR1.137 on cells expressing CXCR4-F249L mutant. Elaborate on the closer interaction suggested between the triazole group of AGR1.137 and the F249 residue

At the reviewer’s suggestion, Fig. 5 has been modified to incorporate a closer view of the interactions identified and new panels in new Fig. 6 have been added to show in detail the effect of the mutations selected on the structure of the cleft between TMV and TMVI. The main difference between AGR1.135 and AGR1.137 is how the triazole group interacts with F249 and L216 (Author response image 6). In AGR1.137, the three groups are aligned in a parallel organization, which appears to be more effective: This might be due to a better adaptation of this compound to the cleft since there is only one hydrogen bond with V124. In AGR1.135, the compound interacts with the phenyl ring of F249 and has a stronger interaction at the apical edge to stabilize its position in the cleft. However, there is still an additional interaction present. When changing F249

Author response image 6.

Cartoon representation of the interaction of CXCR4 F249L mutant with AGR1.135 (A) and AGR1.137 (B). The two most probable conformations of Leucine rotamers are represented in cyan A and B conformations. Van der Waals interactions are depicted in blue cyan dashed lines, hydrogen bonds in black dashed lines. CXCR4 segments of TMV and TMVI are colored in blue and pink, respectively

to L (Fig. VIIA, B, only for review purposes) and showing the two most likely rotamers resulting from the mutation, it is observed that rotamer B is in close proximity to the compound, which may cause the binding to either displace or adopt an alternative conformation that is easier to bind into the cleft. As previously mentioned, it is likely that AGR1.135 can displace the mutant rotamer and bind into the cleft more easily due to its higher affinity.

(47) In the "Materials and Methods" section, the computational approach for the "discovery of CXCR4 modulators" requires significant revision and clarification. The following suggestions aim to address the identified issues: 1. Structural Modeling: 

-Reconsider the use of SWISS-MODEL if there is an available PDB code for the entire CXCR4 structure. Clearly articulate the rationale for choosing one method over the other and explain any limitations associated with the selected approach. 

The SWISS-model server allows for automated comparative modeling of 3D protein structures that was pioneered in the fields of automated modeling. At the time we started this project. it was the most accurate method to generate reliable 3D protein structure models.

As explained above, we have now predicted the structure of the target using AlphaFold (Jumper J. et al, Nature 2021) and performed several additional experiments that confirm that the small compounds bind the selected pocket as the original strategy indicated (see our response to point 6). (Fig. II, only for review purposes).

(48) 2. Parametriza7on of Small Compounds: 

-Provide a detailed description of the parametrization process for the small compounds used in the study. Specify the force field and parameters employed, considering the obsolescence of AMBER14 and ff14SB. Consider adopting more contemporary force fields and parameterization strategies. 

When we performed these experiments, some years ago, the force fields applied (ff14SB, AMBER14 used in MD or OPLS2004 in docking with Glide) were well accepted and were gold standards. It is, however, true that the force fields have evolved in the past few years, Moreover, in the case of the MD simulations, to consider the parameters of the ligands that are not contained within the force field, we performed an additional parameterization as a standard methodology. We then generated an Ab initio optimization of the ligand geometry, defining as basis sets B3LYP 6-311+g(d), using Gaussian 09, Revision A.02, and then a single point energy calculation of ESP charges, with HF 6311+g(d) on the optimized structure. As the last step of the parametrization, the antechamber module was used to adapt these charges and additional parameters for MD simulations.

(49) 3. Treatment of Lipids and Membrane: 

-Elaborate on how lipids were treated in the system. Clearly describe whether a membrane was included in the simulations and provide details on its composition and structure. Address the role of the membrane in the study and its relevance to the interactions between CXCR4 and small compounds 

To stabilize CXCR4 and more accurately reproduce the real environment in the MD simulation, the system was embedded in a lipid bilayer using the Membrane Builder tool (Sunhwan J. et al. Biophys. J. 2009) from the CHARMM-GUI server. The membrane was composed of 175 molecules of the fatty acid 1-palmitoyl-2-oleoyl-sn-glycero-3phosphocholine (POPC) in each leaflet. The protein-membrane complex was solvated with TIP3 water molecules. Chloride ions were added up to a concentration of 0.15 M in water, and sodium ions were added to neutralize the system. This information was previously described in detail.

(50) 4. Molecular Dynamics Protocol: 

-Provide a more detailed and coherent explanation of the molecular dynamics protocol. Clarify the specific steps, parameters, and conditions used in the simulations. Ensure that the protocol aligns with established best practices in the field.

Simulations were calculated on an Asus 1151 h170 LVX-GTX-980Ti workstation, with an Intel Core i7-6500 K Processor (12 M Cache, 3.40 GHz) and 16 GB DDR4 2133 MHz RAM, equipped with a Nvidia GeForce GTX 980Ti available for GPU (Graphics Processing Unit) computations. MD simulations were performed using AMBER14 (Case D.A. et al. AMBERT 14, Univ. of California, San Francisco, USA, 2014) with ff14SB (Maier J.A. et al. J. Chem. Theory Comput. 2015) and lipid14 (Dickson C. J. et al. J. Chem. Theory Comput. 2014) force fields in the NPT thermodynamic ensemble (constant pressure and temperature). Minimization was performed using 3500 Steepest Descent steps and 4500 Conjugate Gradient steps three times, firstly considering only hydrogens, next considering only water molecules and ions, and finally minimizing all atoms. Equilibration raises system temperature from 0 to 300 K at a constant volume fixing everything but ions and water molecules. After thermalization, several density equilibration phases were performed. In the production phase, 50 ns MD simulations without position restraints were calculated using a time step of 2 fs. Trajectories of the most interesting poses were extended to 150 ns. All bonds involving hydrogen atoms were constrained with the SHAKE algorithm (Lippert R.A. et al. J. Chem. Phys. 2007). A cutoff of 8 Å was used for the Lennard-Jones interaction and the short-range electrostatic interactions. Berendsen barostat (Berendsen H.J. et al. J. Chem. Phys.  1984) and Langevin thermostat were used to regulate the system pression and temperature, respectively. All trajectories were processed using CPPTRAJ (Roe D.R. & Cheatham III T.E. J. Chem. Theory Comput. 2013) and visualized with VMD (Visual Molecular Dynamics) (Humphrey W. et al. J. Mol. Graphics. 1996). To reduce the complexity of the data, Principal Component Analysis (PCA) was performed on the trajectories using CPPTRAJ.

(51) Consider updating the molecular dynamics protocol to incorporate more contemporary methodologies, considering advancements in simulation techniques and software.

In our answer to points 6 and 47, we describe why we use the technology based on Swiss-model and PELE analysis and how we have now used Alphafold and other more contemporary methodologies to confirm that the small compounds bind the selected pocket.

(52) Figure 1A: 

•  Consider switching to a cavity representation for CXCL12 to enhance clarity and emphasize the cleft.

Fig. 1A has been modified to emphasize the cleft.

(53) Explicitly show the TMV-TMVI cleft in the figure for a more comprehensive visualization. 

In Fig. 1A we have added an insert to facilitate TMV-TMVI visualization.

(54) Figure 1B: 

•  Clearly explain the meaning of the second DMSO barplot to avoid confusion. 

To clarify this panel, we have modified the figure and the figure legend. Panel B now includes a complete titration of the three compounds analyzed in the manuscript.  The first bar shows cell migration in the absence of both treatment with AMD3100 and stimulation with CXCL12.  The second bar shows migration in response to CXCL12 in the absence of AMD3100. The third bar shows the effect of AMD3100 on CXCL12-induced migration, as a known control of inhibition of migration.  We hope that this new representation of the data results is clearer.

(55) Figure 1C: 

•  Provide a clear legend explaining the significance of the green shading on the small compounds. 

The legend for Fig. 1C has been modified accordingly to the reviewer’s suggestion.

(56) Figure 2: 

•  Elaborate on the role of fibronectin in the experiment and explain the specific contribution of CD86-AcGFP.

The ideal situation for TIRF-M determinations is to employ cells on a physiological substrate complemented with or without chemokines. Fibronectin is a substrate widely used in different studies that allows cell adhesion, mimicking a physiological situation. Jurkat cells express alpha4beta1 and alpha5beta1 integrins that mediate adhesion to fibronectin (Seminario M.C. et al. J. Leuk. Biol. 1999).

Regarding the use of CD86-AcGFP in TIRF-M experiments. We currently determine the number of receptors in individual trajectories of CXCR4 using, as a reference, the MSI value of CD86-AcGFP that strictly showed a single photobleaching step (Dorsch S. et al. Nat Methods 2009).

We preferred to use CD86-AcGFP in cells instead of AcGFP on glass, to exclude any potential effect on the different photodynamics exhibited by AcGFP when bound directly to glass. In any case, this issue has been clarified in the revised version.

(57) Figure 3D: 

•  Include a plot for the respective band intensity to enhance data presentation 

The plot showing the band intensity analysis of the experiments shown in Fig. 3D was already included in the original version (see old Supplementary Fig. 3). However, in the revised version, we include these plots in the same figure as panels 3E and 3F.  As a control of inhibition of CXCL12 stimulation, we have also included a new figure (Supplementary Fig. 4) showing the effect of AMD3100 on CXCL12-induced activation of Akt and ERK as analyzed by western blot.

(58) Consider adding AMD3100 as a control for comparison. 

In agreement with the reviewer’s suggestion, we have added the effect of AMD3100 in most of the functional experiments performed.

(59) Figure 4: 

•  Address the lack of positive controls in Figure 4 and consider their inclusion for a more comprehensive analysis. 

DMSO bars correspond to the control of the experiment, as they represent the effect of CXCL12 in the absence of any allosteric modulator. As previously described in this point-by-point reply, DMSO bars correspond to the control performed with the solvent with which the small compounds, at maximum concentration, are diluted.  Therefore, they show the effect of the solvent on CXCL12 responses. In any case, and in order to facilitate the comprehension of the figure we have also added the controls in the absence of DMSO to demonstrate that the solvent does not affect CXCL12-mediated functions, together with the effect of the orthosteric inhibitor AMD3100. In addition, we have also included representative images of the effect of the different compounds on CXCL12-induced polarization (Fig. 4C).

(60) In Figure 4A, carefully assess overlapping error bars and ensure accurate interpreta7on. If necessary, consider alternative representation. 

We have tried alternative representations of data in Fig. 4A, but in all cases the figure was unclear. We believe that the way we represent the data in the original manuscript is the most clear and appropriate.  Nevertheless, we have now included significance values as a table annexed to the figure, as well as the effect of AMD3100, as a control of inhibition

(61) Supplementary Figure 1A: 

•  Improve the clarity of bar plots for better understanding. Consider reordering them from the most significant to the least. 

This was a good idea, and therefore Supplementary Fig. 1A has been reorganized to improve clarity.

(62) Supplementary Figure 1C: 

•  Clarify the rationale behind choosing the 12.5 nM concentration and explain if different concentrations of CXCL12 were tested. 

In old Supplementary Fig. 1C, we used untreated cells, that is, CXCL12 was not present in the assay.  These experiments were performed to test the potential toxicity of DMSO (solvent) or the negative allosteric modulators on Jurkat cells. The 12.5 nM concentration of CXCL12 mentioned in the figure legend applied only to panels A and B, as indicated in the figure legend. We previously optimized this concentration for Jurkat cells using different concentrations of CXCL12 between 5 and 100 nM.  Nevertheless, we have reorganized old supplementary fig. 1 and clarified the figure legend to avoid misinterpretations (see Supplementary Fig 1A, B and Supplementary Fig. 2A, B).

(63) Explain the observed reduction in fluorescence intensity for AGR1.135. 

The cell cycle analysis has been moved from Supplementary Fig. 1C to a new Supplementary Fig. 2.  It now includes the flow cytometry panels to show fluorescence intensity as a function of the number of cells analyzed (Panel 1A) as well as a table (panel B) with the percentage of cells in each phase of the cell cycle. We believe that the apparent reduction in fluorescence that the reviewer observes is mainly due to the number of events analyzed. However, we have changed the flow cytometry panels for others that are more representative and included a table with the mean of the different results. When we determined the percentage of cells in each cell cycle phase, we observed that it looks very similar in all the experimental conditions. That is, none of the compounds affected any of the cell cycle phases. We have also included the effect of H2O2 and staurosporine as control compounds inducing cell death and cell cycle alteration of Jurkat cells.

(64) Supplementary Table 1: 

•  Include a column specifying the scoring for each compound to provide a clear reference for readers. 

To facilitate references to readers, we have now included the inhibitory effect of each compound on Jurkat cell migration in the revised version of this table. 

(65) Minor Points 

Page 2 - Abstract: Rephrase the first sentence of the abstract to enhance fluidity. 

Although the entire manuscript was revised by a professional English editor, we appreciate the valuable comments of this reviewer and we have corrected these issues accordingly.

(66) Page 2 - Abstract: Explicitly define "CXCR4" as "C-X-C chemokine receptor type 4" the first time it appears.

We have not used C-X-C chemokine receptor type 4 the first time it appears in the abstract. CXCR4 is an acronym normally accepted to identify this chemokine receptor, and it is used as CXCR4 in many articles published in eLife. However, we introduce the complete name the first time it appears in the introduction.

(67) Page 2 - Abstract: Explicitly define "CXCL12" as "C-X-C motif chemokine 12" the first time it is mentioned. 

As we have discussed in the previous response, we have not used C-X-C motif chemokine 12 the first time CXCL12 appears in the abstract, as it is a general acronym normally accepted to identify this specific chemokine, even in eLife papers. However, we introduce the complete name the first time it appears in the introduction section.

(68) Page 2 - Abstract: Explicitly define "TMV and TMVI" upon its first mention.

The acronym TM has been defined as “Transmembrane” in the revised version

(69) Page 2 - Abstract: Review the use of "in silico" in the sentence for accuracy and consider revising if necessary.

With the term “in silico” we want to refer to those experiments performed on a computer or via computer simulation software. We have carefully reviewed its use in the new version of the manuscript.

(70) Page 2 - Abstract: Add a comma after "compound" in the sentence, "We identified AGR1.137, a small compound that abolishes...".

A comma after “compound” has been added in the revised sentence.

(71) Page 2 - Significance Statement: Rephrase the first sentence of the "Significance Statement" to avoid duplication with the abstract.

The first sentence of the Significance Statement has been revised to avoid duplication with the abstract. 

(72) Page 2 - Significance Statement: Break down the lengthy sentence, "Here, we performed in silico analyses..." for better readability. 

The sentence starting by “Here, we performed in silico analyses…” has been broken down in the revised manuscript.

(73) Page 2 - Introduction: Replace "Murine studies" with a more specific term for clarity.

The term “murine studies” is normally used to refer to experimental studies developed in mice. We have nonetheless rephrased the sentence.

(74) Page 3 - Introduction: Rephrase the sentence for clarity: "Finally, using a zebrafish model, ..."

The sentence has been now rephrased for clarity.

(75) Results-AGR1.135 and AGR1.137 block CXCL12-mediated CXCR4 nanoclustering and dynamics: 

Rephrase the sentence for clarity: "Retreatment with AGR1.135 and AGR1.137, but not with AGR1.131, substantially impaired CXCL12-mediated receptor nanoclustering.”

The sentence has been rephrased for clarity.

(76) Results - AGR1.135 and AGR1.137 incompletely abolish CXCR4-mediated responses in Jurkat cells: Clarify the sentence: "In contrast to the effect promoted by AMD3100, a binding-site antagonist of CXCR4..."

The sentence has been modified for clarity.

(77) Consider using "orthosteric" instead of "binding-site" antagonist.

The term orthosteric is now used throughout to refer to a binding site antagonist.

(78) Discussion: Use the term "in silico" only when necessary.

We have carefully reviewed the use of “in silico” in the manuscript.

(79) Discussion: Clarify the sentence: "...not affect neither CXCR2-mediated cell migration...". Confirm if "CXCL12" is intended.

The sentence refers to the chemokine receptor CXCR2, which binds the chemokine CXCL2. To test the specificity of the compounds for the CXCL12/CXCR4 axis, we evaluated CXCL2-mediated cell migration.  The results indicated that CXCL2/CXCR2 axis was not affected by the negative allosteric modulators, whereas CXCL12-mediated cell migration was blocked.  The sentence has been clarified in the new version of the manuscript.

(80) Figure 4B: Bold the "B" in the figure label for consistency.

The “B” in Fig. 4B has been bolded.

Reviewer #2

(1) Fig 2. The SPT data is sub-optimal in its presentation as well as analysis. Example images should be shown. The analysis and visualization of the data should be reconsidered for improvements. Graphs with several hundreds, in some conditions over 1000 tracks, per condition are very hard to compare. The same (randomly selected representative set) number of data points should be shown for better visualization. Also, more thorough analyses like MSD or autocorrelation functions are lacking - they would allow enhanced overall representation of the data.

In agreement with the reviewer’s commentary, we have modified the representation of Fig. 2. We have carefully read the paper published by Lord S.J. and col. (Lord S. J. et al., J. Cell Biol. 2020) and we apply their recommendations for these type of data. We have also included as supplementary material representative videos for the TIRF-M experiments performed to allow readers to visualize the original images. Regarding the MSD analyses, they were developed to determine all D1-4 values. According to the data published by Manzo & García-Parajo (Manzo C. & García-Parajo M.F. Rep.Prog. Phys. 2015) due to the finite trajectory length the MSD curve at large tlag has poor statistics and deviates from linearity. However, the estimation of the Diffusion Coefficient (D1-4) can be obtained by fitting of the short tlag region of the MSD plot giving a more accurate idea of the behavior of particles. In agreement we show D1-4 values and not MSD data. 

Due to the space restrictions, it is very difficult to include all the figures generated, but, only for review purposes, we included in this point-by-point reply some representative plots of the MSD values as a function of the time from individual trajectories showing different types of motion obtained in our experiments (Author response image 7).

Author response image 7.

Representative MSD plots from individual trajectories of CXCR4-AcGFP showing different types of motion: A) confined, B) Brownian/Free, C) direct transport of CXCR4-AcGFP particles diffusing at the cell membrane detected by SPT-TIRF in resting JKCD4 cells.

Further analysis, such as the classification based on particle motion, has not been included in this article. This classification uses the moment scaling spectrum (MSS), described by Ewers H. et al. 2005 PNAS, and requires particles with longer trajectories (>50 frames). Only for review purposes, we include a figure showing the percentage of the MSS-based particle motion classification for each condition. As expected, most of long particles are confined, with a slight increase in the percentage upon CXCL12 stimulation in all conditions, except in cell treated with AGR1.137 (Author response image 8).

Author response image 8.

Effects of the negative allosteric modulators on the Types of Motion of CXCR4. Percentage of single trajectories with different types of motion, classified by MSS (DMSO: 58 particles in 59 cells on FN; 314 in 63 cells on FN+CXCL12; AGR1.131: 102 particles in 71 cells on FN; 258in 69 cells on FN+CXCL12; AGR1.135: 86 particles in 70 cells on FN; 120 in 77 cells on FN+CXCL12; AGR1.137: 47 particles in 66 cells on FN; 74 in 64 cells on FN+CXCL12) n = 3.

(2) Fig 3. The figure legends have inadequate information on concentrations and incubation times used, both for the compounds and other treatments like CXCL12 and forskolin. For the Western blot data, also the quantification should be added to the main figure. The compounds, particularly AGR1.137 seem to lead to augmented stimulation of pAKT and pERK. This should be discussed

The Fig. 3 legend has been corrected in the revised manuscript. Fig. 3D now contains representative western blots and the densitometry evaluation of these experiments. As the reviewer indicates, we also detected in the western blot included, augmented stimulation of pAKT and pERK in cells treated with AGR1.137. However, as shown in the densitometry analysis, no significant differences were noted between the data obtained with each compound. As a control of inhibition of CXCL12 stimulation we have included a new Supplementary Fig. 4 showing the effect of AMD3100 on CXCL12-induced activation of Akt and ERK as analyzed by western blot.

(3) Fig. 4 immunofluorescence data on polarization as well as the flow chamber data lack the representative images of the data. The information on the source of the T cells is missing. Not clear if this experiment was done on bilayers or on static surfaces.

Representative images for the data shown in Figure 4B have been added in the revised figure (Fig. 4C). The experiments in Fig. 4B were performed on static surfaces. As indicated in the material and methods section, primary T cell blasts were added to fibronectin-coated glass slides and then were stimulated or not with CXCL12 (5 min at 37ºC) prior to fix permeabilize and stain them with Phalloidin. Primary T cell blasts were generated from PBMCs isolated from buffy coats that were activated in vitro with IL-2 and PHA as indicated in the material and methods section.

(4) The data largely lacks titration of different concentrations of the compounds. How were the effective concentration and treatment times determined? What happens at higher concentrations? It is important to show, for instance, if the CXCR12 binding gets inhibited at higher concentrations. most experiments were performed with 50 uM, but HeLa cell data with 100 uM. Why and how was this determined? 

The revised version contains a new panel in Fig. 1B to show a more detailed kinetic analysis with different concentrations (1-100 µM) of the compounds in the migration experiments using Jurkat cells. We choose 50 µM for further studies as it was the concentration that inhibits 50-75% of the ligand induced cell migration. 

We have also included the effect of two doses of the compounds (10 and 50 µM) in the zebrafish model as well as AMD3100 (1 and 10 µM) as control (new Fig. 7D, E).  Tumors were imaged within 2 hours of implantation and tumor-baring embryos were treated with either vehicle (DMSO) alone, AGR1.131 or AGR1.137 at 10 and 50 µM or AMD3100 at 1 and 10 µM for three days, followed by re-imaging.

Regarding the amount of CXCL12 used in these experiments, with the exception of cell migration assays in Transwells, where the optimal concentration was established at 12.5 nM, in all the other experiments the optimal concentration of CXCL12 employed was 50 nM. In the case of the directional cell migration assays, we use 100 nM to create the chemokine gradient in the device. These concentrations have been optimized in previous works of our laboratory using these types of experiments. It should also be noted that in the experiments using lipid bilayers or TIRF-M experiments, CXCL12 is used to coat the plates and therefore it is difficult to determine the real concentration that is retained in the surface after the washing steps performed prior adding the cells.

(5) The authors state that they could not detect direct binding of the compounds and the CXCR14. It should be reported what approaches were tried and discussed why this was not possible. 

We attempted a fluorescence spectroscopy strategy to formally prove the ability of AGR1.135 to bind CXCR4, but this strategy failed because the compound has a yellow color that interfered with the determinations. We also tried a FRET strategy (see supplementary Fig. 7) and detected a significant increase in FRET efficiency of CXCR4 homodimers in cells treated with AGR1.135; this effect was due to the yellow color of this compound that interferes with FRET determinations. In the same assays, AGR1.137 did not modify FRET efficiency for CXCR4 homodimers and therefore we cannot assume that AGR1.137 binds on CXCR4. All these data have been considered in the revised discussion.

(6) The proliferation data in Supplementary Figure 1 lacks controls that affect proliferation and indication of different cell cycle stages. What is the conclusion of this data? More information on the effects of the drug to cell viability would be important.

Toxicity in Jurkat cells was first determined by propidium iodide incorporation. Some compounds (i.e., AGR1.103 and VSP3.1) were discarded from further analysis as they were toxic for cells. In a deeper analysis of cell toxicity, even if these compounds did not kill the cells, we checked whether they could alter the cell cycle of the cells. New Supplementary Fig. 2 includes a table (panel B) with the percentage of cells in each cell cycle phase, and no differences between any of the treatments tested were detected. 

Nevertheless, to clarify this issue the revised version of the figure also includes H2O2 and staurosporine stimuli to induce cell death and cell cycle alterations as controls of these assays.

(7) The flow data in Supplementary Figure 2 should be statistically analysed. 

Bar graphs corresponding to the old Supplementary Fig. 2 (new Supplementary Fig. 3) are shown in Fig. 3B. We have also incorporated the corresponding statistical analysis to this figure. 

(8) In general, the authors should revise the figure legends to ensure that critical details are added. 

We have carefully revised all the figure legends in the new version of the manuscript.

(9) Bar plots are very poor in showing the heterogeneity of the data. Individual data points should be shown whenever feasible. Superplot-type of representation is strongly advised (https://doi.org/10.1083/jcb.202001064).

We have carefully read the paper published by Lord S.J. and col. (Lord S. J. et al., J. Cell Biol. 2020) and we apply their recommendations for our TIRF-M data (see revised

Fig.  2).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript by Liu et al explores the role of the UPR and immune regulators in the evaluation of nutritional quality in C. elegans. They identify neuronal UPR activation and the MAPK PMK-1 as key responders to low food quality. In particular, the data suggest that these pathways are activated by low levels of vitamin C synthesis that result from the low sugar levels present in heat-killed E. coli.

Strengths:

The results are intriguing and expand our understanding both of physiological food evaluation systems, and of the known roles of stress response pathways in organismal physiology. The authors use a range of techniques, encompassing imaging, metabolomic analysis, gene expression analysis, and behavioural assays, to support their claims.

Thank you for your thorough review and acknowledgment of the strengths of our study.

Weaknesses:

There is limited mechanistic analysis in the study. In particular, how does low vitamin C trigger UPR activation? This is an intriguing finding that, if followed up, could potentially reveal a novel mechanism of UPR activation. In addition, how is the activation of the PMK-1 pathway driven by/coordinated with UPR activation? The data in some figures is not as convincing as it could be: the magnitude of the effect size is small in the supplementation experiments, and the statistical tests used are not always appropriate to enable multiple comparisons.

(1) There is limited mechanistic analysis in the study. In particular, how does low vitamin C trigger UPR activation? This is an intriguing finding that, if followed up, could potentially reveal a novel mechanism of UPR activation. 

Thank you for highlighting the need for further mechanistic analysis in our study. We appreciate the opportunity to clarify the process by which low vitamin C triggers UPR activation.

Our investigation revealed that the vitamin C content in heat-killed E. coli (HK-E. coli) is comparable to that of live E. coli or HK-yfbR mutant E. coli (Figure 4-figure supplement 1A), indicating that the induction of unfolded protein response (UPR) in C. elegans by HK-E. coli is not solely attributed to low vitamin C levels but rather involves other unidentified factors.

Through metabolomic analysis, we observed significant decreases in sugar levels, including lactose, D-(+)-sucrose, and D-(+)-glucose, in HK-E. coli (Figure 3B, Table S1). Notably, supplementing D-(+)-glucose effectively inhibited UPRER, immune response, and avoidance behavior induced by HK-E. coli (Figure 3E-H). These findings suggest that the deficiency in sugars in HK-E. coli triggers a stress response and avoidance behavior in animals, which can be alleviated by D-(+)-glucose supplementation.

Furthermore, when comparing heat-killed E. coli mutant yfbR (HK-yfbR) to HK-E. coli, we observed significantly higher sugar levels, including lactose and D-(+)-sucrose, in HK-yfbR (Figure 3B). This was accompanied by reduced UPRER in animals feeding on HK-yfbR (Figure 3-figure supplement 1B), indicating that higher sugar levels may inhibit the induction of UPRER by low-quality food.

Considering that the synthesis of vitamin C (VC) occurs through the glucuronate pathway, utilizing D-glucose as a precursor 1, 2 (Figure 4A), we investigated whether the vitamin C biosynthesis pathway is involved in evaluating low-quality food using D-glucose. Contrary to our initial hypothesis, animals fed live E. coli did not exhibit higher glucose levels compared to those fed low-quality food (HK_-E. coli_). Our results indicate that animals maintain similar VC levels when fed ideal food (live E. coli) compared to low-quality food (HK-E. coli) (Figure 4B), suggesting that animals do not stimulate VC biosynthesis under favorable food conditions. However, supplementation of D-GlcA or E. coli-yfbR mutation in HK-E. coli significantly improved VC levels when animals were fed low-quality food (HK-OP50) (Figure 4B, 4C). Moreover, VC or D-glucuronate (D-GlcA) supplementation inhibited HK-E. coli-induced UPRER (Figure 4D), indicating that glucose boosts the animal's ability to adapt to unfavorable food environments by increasing VC levels, thereby inhibiting UPRER, but not under favorable food conditions.

These findings shed light on the complex interplay between vitamin C, sugar levels, and UPR activation, providing valuable insights into the mechanisms underlying food evaluation and stress response pathways in organisms.

Overall, we are grateful for the reviewer's constructive feedback, which motivates us to continue our efforts to understanding how the UPR response contributes to the complexities of food evaluation and behavioral responses in organisms.

(2) In addition, how is the activation of the PMK-1 pathway driven by/coordinated with UPR activation?

Thank you for your insightful inquiry. In our discussion section, we have addressed this question by integrating new data and discussion to provide insights into the coordination between PMK-1 pathway activation and UPR activation.

Previous studies have demonstrated that activating innate immunity, specifically the PMK-1 MAPK pathway, results in a reduction in translation3, as well as a shutdown of food digestion in animals4, likely aimed at reducing protein translation and cellular metabolism. To further investigate this relationship, we measured the translation level of animals fed with heat-killed E. coli (HK-E. coli) and found a significant reduction in total translation ability in these animals (Figure 5-figure supplement 1D). This observation suggests that activating innate immunity through the PMK-1 MAPK pathway may serve as a mechanism to slow down translation progress, thereby alleviating the pressure on the unfolded protein response (UPR) and preventing excessive UPRER activation.

By integrating these findings, we propose a model wherein activation of the PMK-1 pathway coordinates with UPR activation to regulate translation and cellular metabolism in response to low-quality food. This coordinated response likely serves to maintain cellular homeostasis and prevent detrimental effects associated with excessive UPRER activation.

These insights contribute to our understanding of the intricate interplay between innate immunity, cellular stress responses, and metabolic regulation in organisms facing nutritional challenges.

(3) The data in some figures is not as convincing as it could be: the magnitude of the effect size is small in the supplementation experiments, and the statistical tests used are not always appropriate to enable multiple comparisons.

We appreciate the reviewers' concerns regarding the data presentation and statistical analyses in some of our figures. In response to this feedback, we have made revisions to improve the robustness and clarity of our statistical methods.

All statistical analyses were conducted using GraphPad Prism 8.0 software. Specifically, a two-tailed unpaired t-test was employed for the statistical analysis of two groups of samples, while one-way or two-way ANOVA was utilized for the statistical analysis of more than two groups of samples. These adjustments ensure appropriate statistical comparisons and enhance the reliability of our findings.

Reviewer #2 (Public Review):

Summary:

In this work, the authors aim to better understand how C. elegans detects and responds to heat-killed (HK) E. coli, a low-quality food. They find that HK food activates two canonical stress pathways, ER-UPR, and innate immunity, in the nervous system to promote food aversion. Through the creative use of E. coli genetics and metabolomics, the authors provide evidence that the altered carbohydrate content of HK food is the trigger for the activation of these stress responses and that supplementation of HK food with sugars (or their biosynthetic product, vitamin C), reduces stress pathway induction and food avoidance. This work makes a valuable addition to the literature on metabolite detection as a mechanism for the evaluation of nutritional value; it also provides some new insight into the physiologically relevant roles of well-known stress pathways in modulating behavior.

Strengths:

-The work addresses an important question by focusing on understanding how the nervous system evaluates food quality and couples this with behavioral change. -The work takes full advantage of the tools available in this powerful system and builds on extensive previous studies on feeding behavior and stress responses in C. elegans.

-Creative use of E. coli genetics and metabolite profiling enabled the identification of carbohydrate metabolism as a candidate source of food-quality signals.

-For the most part, the studies are rigorous and logically designed, providing good support for the authors' model.

We deeply appreciate the reviewer's insightful assessment of our study's strengths. 

Weaknesses:

-It is not clear how the mechanism identified here is connected to previously described, related processes. In particular, it is not clear whether this mechanism has a role in the detection of other low-quality foods. Further, the specificity of the ability of sugar/vitamin C to suppress stress pathway induction is unclear (i.e., does sugar/vitamin C have any effect on the activation of these pathways through other means?). Additionally, the relationship of this pathway to the vitamin B2-sensing mechanism previously described by the senior author is unclear. These issues do not weaken confidence in the authors' conclusions, but they do reduce the potential significance of the work.

(1) In particular, it is not clear whether this mechanism has a role in the detection of other low-quality foods. 

Thank you for your valuable feedback. In response to your inquiry, we investigated whether the UPRER (IRE-1/XBP-1) - Innate immunity (PMK-1/p38 MAPK) axis is specific to evaluating low-quality food (HK-E. coli) or if it plays a broader role in food detection.

We conducted behavioral assays using N2, pmk-1, and xbp-1 mutant animals fed with normal E. coli food, inedible food (Saprophytic staphylococci)4, and pathogenic food (Pseudomonas aeruginosa-PA14)5. We found that N2, pmk-1, and xbp-1 mutant worms did not exhibit avoidance behavior when presented with normal food (OP50). However, both N2 and xbp-1 mutant worms were able to escape from inedible food (N2 was predominantly found on the border areas of the bacterial lawn and xbp-1 mutant worms on border and in), Saprophytic staphylococci, whereas pmk-1 mutant worms did not exhibit this avoidance behavior. Notably, N2 and xbp-1 mutant worms exhibited even more pronounced avoidance behavior when exposed to Pseudomonas aeruginosa, whereas pmk-1 mutant worms were more susceptible to infection by this pathogen (Figure 2-figure supplement 2C). These findings suggest that the UPR-Immunity pathway plays a crucial role in helping animals avoid low-quality food (HK-E. coli) by triggering an avoidance response. In contrast, the Innate immunity pathway, mediated by PMK-1/p38 MAPK, appears to play a key role in evaluating unfavorable food sources, such as HK-E. coli, Saprophytic staphylococci, and Pseudomonas aeruginosa, and helping animals avoid these environments.

(2) Further, the specificity of the ability of sugar/vitamin C to suppress stress pathway induction is unclear (i.e., does sugar/vitamin C have any effect on the activation of these pathways through other means?). 

Thank you for your inquiry regarding the specificity of the ability of sugar/vitamin C to suppress stress pathway induction. We aimed to address this question by investigating whether high levels of VC inhibit other stress-induced UPRER pathways.

Previous studies have shown that both Tunicamycin6 and pathogenic bacteria, such as Pseudomonas aeruginosa-PA145, induce UPRER in C. elegans. In response to your query, we conducted experiments to examine whether VC supplementation inhibits UPRER induced by these stressors. Our findings indicate that VC supplementation does not inhibit UPRER induced by either Tunicamycin or PA14 (Author response image 1).

These results suggest that while sugar/vitamin C may suppress stress pathway induction in the context of low-quality food, its effects may not extend to other stressors that induce UPRER through different mechanisms. This insight helps clarify the specificity of sugar/vitamin C's role in modulating stress pathway activation, contributing to a better understanding of the broader regulatory networks involved in stress response in C. elegans.

Author response image 1.

VC supplementation does not inhibit Tunicamycin or PA14-induced UPRER.

(3) Additionally, the relationship of this pathway to the vitamin B2-sensing mechanism previously described by the senior author is unclear.

In response to your comment, we would like to clarify the relationship of our pathway to the previously described vitamin B2-sensing mechanism we found. Previous studies have demonstrated that heat-killed E. coli (HK-E. coli) serves as a low-quality food source incapable of supporting the growth of C. elegans larvae, whereas supplementation with vitamin B2 (VB2) can restore animal growth7

This study investigates the role of sugar deficiency in HK-E. coli, which induces the UPRER-immune response and avoidance behavior in C. elegans. Surprisingly, our findings indicate that supplementing HK-E. coli with carbohydrates such as D-Glc and D-GlcA does not promote animal development (Figure 3-figure supplement 2G), suggesting that carbohydrates are not essential for supporting animal growth on this food source. However, we did observe that carbohydrates play a critical role in inhibiting the UPRER-immune response induced by sugar deficiency in HK-E. coli.

-The authors claim that the induction of the innate immune pathway reporter irg-5::GFP is "abolished" in pmk-1(RNAi) animals, but Figure S2K seems to show a clear GFP signal when these animals are fed HK-OP50. Similarly, the claim that feeding WT animals HK-OP50 enriches phospho-PMK-1 levels (Fig 2E) is unconvincing - only one western blot is shown, with no quantification, and there is a smear in the critical first lane.

(1) The authors claim that the induction of the innate immune pathway reporter irg-5::GFP is "abolished" in pmk-1(RNAi) animals, but Figure S2K seems to show a clear GFP signal when these animals are fed HK-OP50. 

We sincerely appreciate the reviewer's attention. To address this concern, we have replaced the images with higher resolution, larger ones in Figure 2-figure supplement 1-I. These updated images provide a clearer representation of the data, ensuring that all details are readily visible and enabling a more accurate interpretation of the results.

(2) Similarly, the claim that feeding WT animals HK-OP50 enriches phospho-PMK-1 levels (Fig 2E) is unconvincing - only one western blot is shown, with no quantification, and there is a smear in the critical first lane.

Thank you, following reviewer’s suggestion, we also repeated some of the western. We now replace the Figure 2E and quantified relative intensity of pPMK-1/tublin. We also provide the uncropped western blots images as source data ( “raw-data WB” file). 

-The rationales for some of the paper's hypotheses could be improved. For example, the rationale for screening the E. coli mutant library is that some mutants, when heat-killed, may be missing a metabolite that induces the ER-UPR. A more straightforward hypothesis might be that some mutant E. coli strains aberrantly induce the ER-UPR when *not* heat-killed, because they are missing a metabolite that prevents stress pathway induction. This is not in itself a major concern, but it would be useful for the authors to provide a rationale for their hypothesis.

Thank you for the insightful suggestion. We acknowledge the importance of providing a clear rationale for our hypotheses in the paper. In response to this feedback, we have enhanced the discussion section to better elucidate the rationale behind our hypotheses.

One limitation of our study is the lack of explanation for why HK-E. coli activates UPRER and immunity. We hypothesized that when heat-killed, HK-E. coli may lack or contain altered levels of certain metabolites that either activate or inhibit UPRER and immunity, respectively. Additionally, we speculated that E. coli mutants killed by heat may lack metabolites that activate UPRER and immunity, or conversely, have increased levels of metabolites that inhibit these pathways.

Fortunately, our investigation led to the discovery of the E. coli mutant yfbR, which inhibits UPRER and immunity by increasing carbohydrates that aid in resisting these stress pathways. Moving forward, we intend to further explore the intricate relationship between HK-E. coli and UPRER-immunity. This will be a key focus of our future research efforts.

-The authors do not provide any explanation for some unexpected results from the E. coli screen. Earlier in the paper, the authors found that innate immune signaling is downstream of ER-UPR activation. However, of the 20 E. coli mutants that, when heat-killed, "did not induce... the UPR-ER reporter," 9 of them still activate the innate immune response. This seems at odds with the authors' simple model since it suggests that low-quality food can induce innate immune signaling independently of the ER-UPR. Further, only one of the 9 has an effect on behavior, even though failure to activate the innate immune pathway might be expected to lead to a behavioral defect in all of these.

Thank you for your understanding, and we apologize for any confusion caused by our earlier statement. To provide clarification, our study revealed that out of the 20 E. coli mutants examined, none activated the UPRER. Among these mutants, 9 did not induce immunity, and interestingly, one out of these 9 mutants demonstrated the ability to inhibit avoidance behavior.

This diversity in phenotypic outcomes can be attributed to the varied metabolites present in different E. coli mutants. To thoroughly evaluate the effects of these mutants, we conducted a comprehensive three-step screening process, utilizing UPRER marker, immunity marker, and avoidance behavior assays.

Through this rigorous approach, we identified the E. coli mutant, yfbR, which exhibited the desired inhibitory effects on UPRER, immunity, and avoidance behavior.

Subsequently, we conducted a metabolomics analysis of various food qualities (HK-K12, HK-yfbR, and Live-K12). Our findings revealed higher sugar levels in

HK-yfbR and Live-K12 compared to HK-K12 (Figure 3B, Figure 3-figure supplement 2A, and Table S1), indicating that sugar deficiency might trigger the UPRER, immunity responses, and subsequent avoidance behavior. 

-In a number of places, the writing style can make the authors' arguments difficult to follow.

Thanks for the reviewer’s efforts. We changed all of these errors and polish the language of this paper. 

-Some of the effect sizes observed by the authors are exceedingly small (e.g, the suppression of hsp-4::gfp induction by sugar supplementation in Figs 3C-E), raising some concern about the biological significance of the effect.

Thank you for your feedback. In response to your concern, we have included additional clarification in the manuscript.

We have added the following statement: “While sugar effectively inhibits the HK-E. coli-induced UPRER and immune response, it does not fully suppress it to the extent observed with live-E. coli (Figure 3C-F). This implies that additional nutrients present in live-E. coli might also contribute to the inhibition of UPRER and immune response.”

This addition helps to address the observation that some effect sizes appear small, providing context and suggesting potential factors that may influence the outcomes. 

-In some cases, there is a discrepancy between the fluorescence images and their quantitation (e.g., Figure 3E, where the effect of glucose on GFP fluorescence seems much stronger in the image than in the graph).

Thank you for your valuable suggestion. In response, we have revised our image selection process to ensure impartiality. We now randomly select images to ensure they accurately represent the quantified data without bias. More details regarding this update can be found in Author response image 2.

Author response image 2.

More original picture corresponding to Figure 3E 

Reviewer #3 (Public Review):

Summary:

Animals can evaluate food quality in many ways. In contrast to the rapid sensory evaluation with smell and taste, the mechanism of slow nutrient sensation and its impact on food choice is unexplored. The authors utilize C. elegans larvae and their bacterial food as an elegant model to tackle this question and reveal the detailed molecular mechanism to avoid nutrient-poor foods.

Strengths:

The strength of this study is that they identified the molecular identities of the critical players in bacterial food and C. elegans using unbiased approaches, namely metabolome analysis, E. coli mutant screening, and RNA sequencing. Furthermore, they strengthen their findings by thorough experiments combining multiple methods such as genetics, fluorescent reporter analysis, and Western blot.

Thank you for highlighting the strengths of our study. 

Weaknesses:

The major caveat of this study is the reporter genes. The transcriptional reporters were used to monitor the UPRER and immune responses in the intestine of C. elegans.

However, their tissue-specific rescue experiments suggest that the genes in the UPRER and immune response function in the neurons. Thus, we should carefully interpret the results of the reporter genes.

Thank you for your insightful comment. We appreciate the opportunity to address your concerns regarding the interpretation of our reporter gene data.

Upon reevaluation, we observed strong induction of the UPRER reporter

(Phsp-4::GFP)8 and immunity reporter (Pirg-5::GFP)9 both in the intestine (Figure 1F-G) and in neurons (Figure 1-figure supplement 2A) in response to feeding unfavorable food (HK-E. coli). This suggests that both the UPRER and immune pathways may indeed respond to low-quality food (HK-E. coli) in multiple tissues of C. elegans. While we acknowledge that our tissue-specific rescue experiments suggest a role for these pathways in neurons, the intestinal fluorescence of Phsp-4::GFP or Pirg-5::GFP is easily observable and scorable. Therefore, we chose to focus our further analyses on the intestine for practical reasons.

Overall, this work provides convincing data to support their model. In the C. elegans field, the behaviors of larvae are not well studied compared to adults. This work will pose an interesting question about the difference between larvae and adults in nutrition sensing in C. elegans and provide a framework and candidate molecules to be studied in other organisms.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major suggestions:

(1) My major overall comment is that the paper would be substantially strengthened by more mechanistic analysis. In particular, how does low vitamin C trigger UPR activation? This is an intriguing finding and it would be important to see it more fully explored.  

Our study revealed that the vitamin C content in HK_-E. coli_ is comparable to that of live E. coli or HK-yfbR (Figure 4-figure supplement 1A), suggesting that the induction of unfolded protein response (UPR) in C. elegans by HK-E. coli is not attributed to low vitamin C levels, but rather to unknown factors.

Metabolomic analysis showed that the sugar levels, including lactose, D-(+)-sucrose, and D-(+)-glucose, were significantly decreased in HK-E. coli (Figure 3B, Table S1).

Furthermore, we found that supplementing D-(+)-glucose effectively inhibited UPRER (Figure 3E), immune response (Figure 3F, 3G, and Figure 3-figure supplement 2D), and avoidance behavior (Figure 3H) induced by HK-E. coli. Our findings suggest that the deficiency in sugars in HK-E. coli triggers a stress response and avoidance behavior in animals, which can be alleviated by D-(+)-glucose supplementation.

Notably, when E. coli was heat-killed, we observed that the sugar levels, including lactose and D-(+)-sucrose, were significantly higher in the heat-killed E. coli mutant yfbR (HK-yfbR) compared to HK-E. coli (Figure 3B). Moreover, we found that UPRER was reduced in animals feeding HK-yfbR (Figure 3-figure supplement 1B), indicating that higher sugar levels may inhibit the induction of UPRER by low-quality food.

The synthesis of vitamin C (VC) occurs through the glucuronate pathway, utilizing D-glucose as a precursor 1, 2 (Figure 4A). This led us to investigate whether the vitamin C biosynthesis pathway is involved in evaluating low-quality food by using D-glucose. In this study, we found that animals feeding live E. coli, which should produce more VC, exhibit higher glucose levels. However, our results show that animals maintain similar VC levels when fed ideal food (live E. coli) compared to low-quality food (HK-E. coli) (Figure 4B), suggesting that animals do not stimulate VC biosynthesis under favorable food conditions. In contrast, when animals are fed low-quality food (HK-OP50), we found that supplementing D-GlcA (Figure 4C) or E. coli-yfbR mutation (Figure 4B) in HK-E. coli can improve VC levels. Moreover, we found that VC or D-glucuronate (D-GlcA) supplementation inhibited HK-E. coli induced UPRER (Figure 4D). These data indicate that glucose boosts the animal's ability to adapt to unfavorable food environments by increasing VC levels, thereby inhibiting UPRER, but not in favorable food conditions.

In addition,we asked whether high level of VC inhibits other stress induced UPRER. Previous study shown that Tunicamycin6 and pathogenic bacteria-Pseudomonas aeruginosa-PA145 induce UPRER in C. elegans. We found that VC supplementation does not inhibit Tunicamycin or PA14-induced URPER (Author response image 3). 

Author response image 3.

VC supplementation does not inhibit Tunicamycin or PA14-induced UPRER.

In addition, how is the activation of the PMK-1 pathway driven by/coordinated with UPR activation? 

If the authors do not want to pursue these directions experimentally in this study, the discussion would be strengthened by considering these questions and identifying candidate regulatory mechanisms for further exploration.

In this study, we found that heat-killed E. coli (HK-E. coli), a low-sugar food, triggers cellular unfolded protein response (UPRER) and immune response. We also demonstrated that 1) the activation of UPRER by low-quality food depends on the IRE-1/XBP-1, 2) activation of immune response (PMK-1) is downstream of XBP-1 in responding to low-quality food.

how is the activation of the PMK-1 pathway driven by/coordinated with UPR activation? 

In our discussion part, we added new data and discussion to answer reviewer’s question. 

A previous study has shown that activating innate immunity (PMK-1 MAPK) leads to a reduction in translation 3. Our own previous research has also demonstrated that PMK-1 activation causes a shutdown of food digestion in animals4, likely to reduce protein translation and cellular metabolism. To investigate this further, we measured the translation level of animals fed with HK-E. coli and found that total translation ability is significantly reduced in these animals (Figure 5-figure supplement 1D). This finding suggests that activating innate immunity (PMK-1 MAPK) may serve as a mechanism to slow down translation progress, thereby alleviating the pressure on the unfolded protein response (UPR) and preventing excessive UPRER activation.

(2) Figure 2C: The data shows that xbp-1 mutants are significantly more likely to leave heat-killed E. coli. However, no other conditions are examined. Is this avoidance defect specific to heat-killed E. coli, or is it a more general effect of xbp-1 mutants - that is, are other conditions that evoke avoidance also affected by mutation of xbp-1? Is feeding behavior on regular E. coli altered in this background? The finding would be more relevant if the authors could clarify or provide more context for their claims here.

We then asked whether UPRER (IRE-1/XBP-1) - Innate immunity (PMK-1/p38 MAPK) axis is specific to evaluate low-quality food (HK-E. coli). We examined the avoidance behavior phenotype of wild-type and mutant L1 animals by placing them on various food conditions, including normal E. coli food, inedible food (Saprophytic staphylococci) and pathogenic food (Pseudomonas aeruginosa-PA14), for a 24-hour period. We found that N2, pmk-1, and xbp-1 mutant worms did not exhibit avoidance behavior when presented with normal food (OP50). However, both N2 and xbp-1 mutant worms were able to escape from inedible food, Saprophytic staphylococci, whereas pmk-1 mutant worms did not show this avoidance. Notably, xbp-1 mutant worms exhibited even more pronounced avoidance behavior when exposed to Pseudomonas aeruginosa, whereas pmk-1 mutant worms were more susceptible to infection by this pathogen (Figure 2-figure supplement 2C). These findings suggest that the UPR-Immunity pathway plays a crucial role in helping animals avoid low-quality food by triggering an avoidance response. In contrast, the Innate immunity pathway, which is mediated by PMK-1/p38 MAPK, appears to play a key role in evaluating unfavorable food sources, such as HK-E. coli, Saprophytic staphylococci, and Pseudomonas aeruginosa, and helping animals avoid these environments.

(3) Figure 3C-F: The magnitude of the changes between conditions shown in these panels is small. To what extent does this supplementation represent a full rescue? The findings would be strengthened if figures/images for the control condition (non-HK E. coli) were shown for comparison to allow the reader to assess the extent to which UPR/PMK-1 activation is rescued.

In response to a reviewer's suggestion, we included live-E. coli as a control in our study. Notably, our data revealed that the addition of lactose, D-(+)-sucrose, and D-(+)-glucose partially inhibited the HK-E. coli-induced unfolded protein response (UPRER) and immune response, suggesting that other nutrients present in live-E. coli may also play a role in inhibiting UPRER.

We added this in manuscript: “While sugar effectively inhibits the HK-E. coli-induced UPRER and immune response, it does not fully suppress it to the extent observed with live-E. coli (Figure 3C-F). This implies that additional nutrients present in live-E. coli might also contribute to the inhibition of UPRER and immune response.” 

(4) Figure 5B-D: The magnitude of changes shown between conditions here again appear to be very small, even those labelled as statistically significant. It is important to ensure that the correct statistical tests have been used to assess the significance of these differences (see below).

All statistical analyses were performed in Graphpad prism 8.0. Two-tailed unpaired t test was used for statistical analysis of two groups of samples，one-way or two-way ANOVA was used for statistical analysis of more than two groups of samples.

(5) Methods: In the "Statistical analysis" section, the authors state that "All statistical analyses were performed using Student's t-test". However, this is not the appropriate test to use in experiments where multiple comparisons are made, which is true in several instances across the paper. In these cases, a more appropriate statistical test should be used.

All statistical analyses were performed in Graphpad prism 8.0. Two-tailed unpaired t test was used for statistical analysis of two groups of samples，one-way or two-way ANOVA was used for statistical analysis of more than two groups of samples.

Minor suggestions:

(1) Figure S2: RNAi is usually delivered in a different E. coli strain, HT115. Is this the case with the RNAi knockdowns in Figure S2, and given that diet can influence UPR activation, is it possible that this different diet could change the phenotypes observed?

This should be clarified by the authors.

In this study, all RNAi experiments involved bleaching adult animals under RNAi strain culture conditions to obtain L1 animals. Subsequently, L1 animals were transferred to HK-E. coli OP50 for phenotype analysis. In response to a reviewer's suggestion, we observed that L1 animals obtained from mothers fed E. coli strains OP50, HT115, or K12 exhibited similar UPR induction under HK-E. coli OP50 feeding conditions (Author response image 4). These findings suggest that variations in diet did not alter the UPR phenotypes.

Author response image 4.

L1 animals obtained from mothers fed E. coli strains OP50, HT115, or K12 exhibited similar UPR induction under HK-E. coli OP50 feeding conditions 

Reviewer #2 (Recommendations For The Authors):

Line 182: "irg-5::GFP" should be "hsp-4::gfp".

Thanks for the reviewer’s efforts. We have changed this error.

Reviewer #3 (Recommendations For The Authors):

Major comments:

(1) The reporter genes of UPRER and immune response were analyzed in the intestine throughout the study. On the other hand, their rescue experiments suggest that these pathways function in the neurons. They should provide the fluorescence data in the neurons at least for Figures 1F and 1G to confirm that the intestinal response matches the neuronal response and mention that further analyses were done in the intestine for easy scoring.

Consistent with the results of the RNA sequencing (RNA-seq) analysis, the UPRER reporter (Phsp-4::GFP)8 and immunity reporter (Pirg-5::GFP)9 were strongly induced in intestinal (Figure 1F-G) and neurons (Figure 1-figure supplement 2A) by feeding unfavorable food (HK-E. coli), suggesting that UPRER and immune pathways may respond to low-quality food (HK-E. coli). As intestinal fluorescence (Phsp-4::GFP or Pirg-5::GFP) is easy observation and scoring, the further analyses were done in the intestine. 

(2) I have concerns about the interpretation of the p-PMK-1 data. Although the authors described that "p-PMK-1 is prominently increased" in the text (Line 150), it is unclear on the data (Figure 2E). Similarly, the authors' statement "p-PMK-1 is decreased in animals with D-GlcA (F).." was not fully supported by the data in Figure 4F. The experiment should be repeated and quantified. Moreover, pPMK-1 showed single bands in Figure 2E, but double bands in Figure 3G, 4F, and 4G. The authors should explain why that is the case and which band we should look at for Figures 3G, 4F, and 4G.

As reviewer’s suggestion, we also repeated some of the western. We found that after longer expose, there are two bands for pPMK-1 (Figure 2E, new data; and “raw-data WB” file). The VHP-1 phosphatase is known to inhibit PMK-13. In our previous study, we found that worms treated with vhp-1(RNAi), which hyperactivates p-PMK-1 (lower band) 4. In contrast, the two bands are disappeared in pmk-1 mutant (Author response image 5). Thus, the lower band indicates the pPMK-1. We now replace the Figure 2E and quantified relative intensity of pPMK-1/tublin. We also provide the uncropped western blots images as source data ( “raw-data WB” file). 

Author response image 5.

In our previous study, we found that worms treated with vhp-1(RNAi), which hyperactivates p-PMK-1 (lower band) 4. In contrast, the two bands are disappeared in pmk-1 mutant. These pictures are extracted from our previous study4.

(3) Heat-killed E. coli (HK-E. coli) is low-quality because the lack of sugar cannot support the growth of C. elegans larvae (Qi and Han, Cell, 2018). Thus, animals do not show the UPRER-immune response and avoidance when HK-E. coli is supplemented with sugars such as glucose (Line 225-227). If these sugars are the key, C. elegans larvae should be able to grow better with HK-E. coli supplemented with glucose. Authors should address this possibility.

Previous studies have shown that heat-killed E. coli (HK-E. coli) is a low-quality food source that cannot support the growth of C. elegans larvae7. Here, we found that sugar deficiency in HK-E. coli induces the UPRER-immune response and avoidance behavior in C. elegans. Given this, we investigated whether sugar supplementation could promote animal growth when fed HK-E. coli. To our surprise, supplementing HK-E. coli with carbohydrates (D-Glc, D-GlcA) did not support animal development (Figure 3-figure supplement 2G), suggesting that carbohydrates are not essential for supporting animal growth on this food source. However, we did find that carbohydrates are critical for inhibiting the UPRER-immune response induced by sugar deficiency in HK-E. coli.

(4) Line 884: Instead of the Student's t-test, the ANOVA should be used for multiple comparisons.

All statistical analyses were performed in Graphpad prism 8.0. Two-tailed unpaired t test was used for statistical analysis of two groups of samples，one-way or two-way ANOVA was used for statistical analysis of more than two groups of samples.

(5) Although the results are interesting and convincing, the manuscript needs some careful editing and proofreading. As far as I could catch, there are more than 100 errors and typos, as I summarized in minor comments. I recommend the authors proofread thoroughly to make this work easier to read.

Thanks for the reviewer’s efforts. We changed all of these errors and polish the language of this paper. 

Minor comments:

(1) Line 30: nature -> natural

(2) Line 86: elegnas -> elegans

(3) Line 93: the17h -> the 17h

(4) Line 97: response -> respond

(5) Line106: responded -> respond

(6) Lien 107-109: Add references for the three reporters

(7) Line 114: immune -> immune pathway

(8) Line 118: immune depended -> immune-dependent

(9) Line 128, 594, 596: deferentially -> differentially

(10) Line 131: Explain what IRE-1-mediated splicing of xbp-1 with references

(11) Line 170: XPB-1 -> XBP-1

(12) Line 179: URP -> UPR

(13) Line 181: hsp-4::GFP -> Phsp-4::GFP

(14) Line 183: Italicize E. coli; mutant -> mutants

(15) Line 184: irg-5::GFP -> Pirg-5::GFP (2 places)

(16) Line 197, 203, 206, 207: Lactose -> lactose

(17) Line 206, 209, 217, 225, 228, 232, 237, 262, 442, 445, 604, 739: Glucose -> glucose

(18) Line 218: Sugars deficiency -> sugar deficiency

(19) Line 229: found contribute to -> found to contribute to

(20) Line 235, 537, 539, 587, 599, 642, 855: Italicize E. coli

(21) Line 236: same -> the same

(22) Line 239: I recommend adding "in C. elegans". This study uses both E. coli and C.

elegans genetics. Sometimes, it is confusing which organism was mentioned. It should be applied where it is necessary.

(23) Line 240: additional -> addition

(24) Line 339, 642: Italicize kgb-1

(25) Line 390: Italicize Pseudomonas aeruginosa, Bacillus thuringiensis,

Staphylococcus aureus, and Serratia marcescens

(26) Line 394: wiht -> with

(27) Line 400, 550: Change ER to superscript; Italicize ire-1, xbp-1, and pmk-1

(28) Line 415: xpb-1 -> xbp-1

(29) Line 460, 525, 531, 532, 617, 655: Italicize yfbR

(30) Line 457, 468, 472, 475, 482, 497, 513, 624, 629, 633, 733. 758: Vitamin -> vitamin

(31) Line 459: Make it clear what is the relationship between vitamin C and TAA

(32) Line 527: Do not italicize mutant

(33) Line 538: Phsp-6:GFP -> Phsp-6::GFP (to match other descriptions)

(34) Line 540: Phsp-4:GFP -> Phsp-4::GFP (to match other descriptions)

(35) Line 540: Italicize hsp-4

(36) Line 543: Pirg-5:GFP -> Pirg-5::GFP (to match other descriptions) and italicize irg-5

(37) Line 550, 881: Innate -> innate

(38) Line 557, 560, 564, 838: Do not italicize HK

(39) Line 561: Remove the extra space before "three"

(40) Line 575, 577: Reporter -> reporter

(41) Line 575, 607: Italicize Phsp-4::GFP

(42) Line 577: immunity -> Immunity; Italicize Pirg-5::GFP

(43) Line 585, 653: keio -> Keio

(44) Line 586: hsp-4::GFP -> Phsp-4::GFP

(45) Line 586, 589 (2 places): irg-5::GFP -> Pirg-5::GFP

(46) Line 597: Remove "all"

(47) Line 600: Trehalose -> trehalose

(48) Line 609: Italicize Pirg-5::GFP

(49) Line 615: critically -> critical

(50) Line 636: Remove "+"

(51) Line 656 (2 places), 682: Do not italicize OP50

(52) Line 664: Lead -> lead

(53) Line 681: Describe the composition of NGM or show the reference. Since this paper examines nutrition, the composition of the medium is crucial.

(54) Line 686-706: Italicize all allele names. Be consistent with how to write the promoter to avoid confusion (e.g., ttx-3p -> Pttx-3). Be consistent with how to describe the transgene (e.g., Phsp-4::GFP(zcIs4) -> zcIs4[Phsp-4::GFP])

(55) Line 710: Describe the composition of LB or show the reference. Since this paper examines nutrition, the composition of the medium is crucial.

(56) Line 709, 856 (2 places), 858: Do not italicize K12 to make it consistent

(57) Line 719: Podr-1p:RFP -> Podr-1::RFP

(58) Line 722, 724: Italicize ges-1 and xbp-1

(59) Line 723: Pges-1:xbp-1::GFP -> Pges-1::xbp-1::GFP

(60) Line 735: Glucuronic -> glucuronic

(61) Line 748: I believe it is 5 mm instead of 0.5 mm

(62) Line 750: The equation should be (5 mm)2/(17.5 mm)2

(63) Line 759: Remove the period after "pattern".

(64) Line 766: Describe how they were synchronized

(65) Line 774: Italicize Psysm-1p::GFP

(66) Line 785: Insert a space before "until"

(67) Line 787: the mutant -> mutant

(68) Line 789, 792, 793, 795 (2 places): GPF -> GFP

(69) Line 791: next -> Next; an -> a

(70) Line 799: Remove a space before "MRC".

(71) Line 804: I do not understand what "until adulthood" means in this context;

Remove a space before "by". (I recommend searching double space and correcting it.)

(72) Line 853: Metabolome -> metabolome

(73) Line 893-1082: Species and gene names should be italicized in Reference

(74) Figures 1F, 1G, S2F, S2G: The panels' order should match the bar graphs' order. The apparent difference in the representative data does not match the marginal difference in the bar graph in Fig. 1G. The authors should double-check the results.

(75) Figure 1F, 2A, 2B, 3C, 3D, 3E, 4D, 4I, S1J, S2A, S2B, S2I, S3B, S3F, S3H: hsp-4::GFP -> Phsp-4::GFP

(76)  Figure 1G, 2D, 3F, 4E, 4J, S1K, S2H, S3C, S3I: irg-5::GFP -> Pirg-5::GFP

(77)  Figure 6: Liquids -> Lipids; Italicize ire-1, xbp-1, pmk-1

(78)  Figure S1I: hsp-6::GFP -> Phsp-6::GFP

(79)  In the legend for Figure S1 after Figure S1, (A), (B)... were duplicated. It is OK in the corresponding main text (Line 530)

(80)  Figure S2F, S3G, S4C, S4D: sysm-1::GFP -> Psysm-1::GFP

(81)  Figure S2G: irg-1::GFP -> Pirg-1::GFP

(82)  Figure S3H and S3I: Describe which ones are Glu + conditions

References: 

(1) Patananan AN, Budenholzer LM, Pedraza ME, Torres ER, Adler LN, Clarke SG. The invertebrate Caenorhabditis elegans biosynthesizes ascorbate. Arch Biochem Biophys 569, 32-44 (2015).

(2) Yabuta Y_, et al. L-Ascorbate Biosynthesis Involves Carbon Skeleton Rearrangement in the Nematode Caenorhabditis elegans. _Metabolites 10,  (2020).

(3) Weaver BP, Weaver YM, Omi S, Yuan W, Ewbank JJ, Han M. Non-Canonical Caspase Activity Antagonizes p38 MAPK Stress-Priming Function to Support Development. Dev Cell 53, 358-369 e356 (2020).

(4) Geng S_, et al. Gut commensal E. coli outer membrane proteins activate the host food digestive system through neural-immune communication. _Cell Host Microbe 30, 1401-1416 e1408 (2022).

(5)  Richardson CE, Kooistra T, Kim DH. An essential role for XBP-1 in host protection against immune activation in C. elegans. Nature 463, 1092-1095 (2010).

(6) Harding HP_, et al. An Integrated Stress Response Regulates Amino Acid Metabolism and Resistance to Oxidative Stress. _Molecular Cell 11, 619-633 (2003).

(7) Qi B, Kniazeva M, Han M. A vitamin-B2-sensing mechanism that regulates gut protease activity to impact animal’s food behavior and growth. eLife 6, e26243 (2017).

(8) Calfon M_, et al. IRE1 couples endoplasmic reticulum load to secretory capacity by processing the XBP-1 mRNA. _Nature 415, 92-96 (2002).

(9) Bolz DD, Tenor JL, Aballay A. A Conserved PMK-1/p38 MAPK Is Required in Caenorhabditis elegans Tissue-specific Immune Response to Yersinia pestis Infection*. The Journal of Biological Chemistry 285, 10832 - 10840 (2010).

Reviewer #2 (Public Review):

Summary:

This paper addresses an important computational problem in learning and memory. Why do related memory representations sometimes become more similar to each other (integration) and sometimes more distinct (differentiation)? Classic supervised learning models predict that shared associations should cause memories to integrate, but these models have recently been challenged by empirical data showing that shared associations can sometimes cause differentiation. The authors have previously proposed that unsupervised learning may account for these unintuitive data. Here, they follow up on this idea by actually implementing an unsupervised neural network model that updates the connections between memories based on the amount of coactivity between them. The authors use their modeling framework to simulate three recent empirical studies, showing that their model captures aspects of these findings that are hard to account for with supervised learning.

Overall, this is a strong and clearly described work that is likely to have a positive impact on computational and empirical work in learning and memory. While the authors have written about some of the ideas discussed in this paper previously, a fully implemented and openly available model is a clear advance that will benefit the field. It is not easy to translate a high-level description of a learning rule into a model that actually runs and behaves as expected. The fact that the authors have made all their code available makes it likely that other researchers will extend the model in numerous interesting ways, many of which the authors have discussed and highlighted in their paper.

Strengths:

The authors succeed in demonstrating that unsupervised learning with a simple u-shaped rule can produce results that are qualitatively in line with the empirical reports. In each of the three models, the authors manipulate stimulus similarity (following Chanales et al.), shared vs distinct associations (following Favila et al.), or learning strength (a stand-in for blocked versus interleaved learning schedule; following Schlichting et al.). In all cases, with hand-tuning of additional parameters, the authors are able to produce model representations that fit the empirical results, but that can't easily be accounted for by supervised learning. Demonstrating these effects isn't trivial and a formal modeling framework for doing so is a valuable contribution. Overall, the work is very thorough. The authors investigate many different aspects of the learning dynamics (learning rate, oscillation strength, hidden layer overlap etc) in these models and produce several key insights. Of particular value are their demonstrations that when differentiation occurs, it occurs very quickly and asymmetrically and results in anti-correlated representations, as well as the distinction between symmetric and asymmetric integration in their model. The authors thoroughly acknowledge the relative difficulty of producing differentiation in their models relative to integration, and are now more clear about why they don't necessarily view this as mismatch with the empirical data. The authors are also more clear about the complicated activation dynamics in their model and why critical ranges for some parameters can't be given -- the number of interacting parameters mean that there are many combinations that could produce the critical activation dynamics and thus the same result. Despite this complexity, the paper is very clearly written; the authors do a good job of both formally describing their model as well as giving readers a high level sense of how many of their critical model components work.

Weaknesses:

Though the u-shaped learning rule is essential to this framework, the paper doesn't do any formal investigation of this learning rule or comparison with other learning rules. The authors do have a strong theoretical interest in this rule as well as experimental precedent for testing this rule, which they now thoroughly discuss in the paper. Still, a stronger argument in support of the non monotonic plasticity hypothesis could have been made by comparing this learning rule to alternatives. Additionally, the authors' choice of strongly prewiring associations makes it difficult to think about how their model maps onto experimental contexts where associations are only weakly learned. However, the authors thoroughly acknowledge why this was necessary and discuss this limitation in the paper.

eLife assessment

This paper presents important computational modeling work that provides a mechanistic account for how memory representations become integrated or differentiated (i.e., having distinct neural representations despite being similar in content). The authors provide convincing evidence that simple unsupervised learning in a neural network model, which critically weakens connections of units that are moderately activated by multiple memories, can account for three empirical findings of differentiation in the literature. The paper also provides insightful discussion on the factors contributing to differentiation as opposed to integration, and makes new predictions for future empirical work.

Reviewer #1 (Public Review):

Ritvo and colleagues present an impressive suite of simulations that can account for three findings of differentiation in the literature. This is important because differentiation-in which items that have some features in common, or share a common associate are less similar to one another than are unrelated items-is difficult to explain with classic supervised learning models, as these predict the opposite (i.e., an increase in similarity). A few of their key findings are that differentiation requires a high learning rate and low inhibitory oscillations, and is virtually always asymmetric in nature.

This paper was very clear and thoughtful-an absolute joy to read. The model is simple and elegant, and powerful enough to re-create many aspects of existing differentiation findings. The interrogation of the model and presentation of the findings were both extremely thorough. The potential for this model to be used to drive future work is huge.

The authors have been very responsive to my previous reviews and I have no further concerns and identify no major weaknesses.

Reviewer #3 (Public Review):

This paper proposes a computational account for the phenomenon of pattern differentiation (i.e., items having distinct neural representations when they are similar). The computational model relies on a learning mechanism of the nonmonotonic plasticity hypothesis, fast learning rate and inhibitory oscillations. In the revised paper, the authors justified the initialization of the model, added empirical evidence supporting the use of two turning points in the NMPH function and provided details of the learning mechanisms of the model. The relatively simple architecture of the model makes its dynamics accessible to the human mind. Furthermore, using similar model parameters, this model produces simulated data consistent with empirical data of pattern differentiation. The authors also provide insightful discussion on the factors contributing to differentiation as opposed to integration.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Ritvo and colleagues present an impressive suite of simulations that can account for three findings of differentiation in the literature. This is important because differentiation-in which items that have some features in common, or share a common associate are less similar to one another than are unrelated items-is difficult to explain with classic supervised learning models, as these predict the opposite (i.e., an increase in similarity). A few of their key findings are that differentiation requires a high learning rate and low inhibitory oscillations, and is virtually always asymmetric in nature.

This paper was very clear and thoughtful-an absolute joy to read. The model is simple and elegant, and powerful enough to re-create many aspects of existing differentiation findings. The interrogation of the model and presentation of the findings were both extremely thorough. The potential for this model to be used to drive future work is huge. I have only a few comments for the authors, all of which are relatively minor.

(1) I was struck by the fact that the "zone" of repulsion is quite narrow, compared with the zone of attraction. This was most notable in the modeling of Chanales et al. (i.e., just one of the six similarity levels yielded differentiation). Do the authors think this is a generalizable property of the model or phenomenon, or something idiosyncratic to do with the current investigation? It seems curious that differentiation findings (e.g., in hippocampus) are so robustly observed in the literature despite the mechanism seemingly requiring a very particular set of circumstances. I wonder if the authors could speculate on this point a bit-for example, might the differentiation zone be wider when competitor "pop up" is low (i.e., low inhibitory oscillations), which could help explain why it's often observed in hippocampus? This seems related a bit to the question about what makes something "moderately" active, or how could one ensure "moderate" activation if they were, say, designing an experiment looking at differentiation.

We thank the reviewer for this comment. In the previous version of the manuscript, in the section entitled “Differentiation Requires a High Learning Rate and Is Sensitive to Activation Dynamics”, we discussed some reasons why differentiation may be more likely to be found in the hippocampus – namely, the high learning rate of the hippocampus and the sparsity of hippocampal activation patterns (pp. 27-28):

“These results have implications for where to look for differentiation in the brain. Our finding that differentiation requires a high learning rate suggests that differentiation will be more evident in the hippocampus than in neocortex, insofar as hippocampus is thought to have a higher learning rate than neocortex (McClelland et al., 1995). In keeping with this prediction, numerous studies have found differentiation effects in hippocampus but not in neocortical regions involved in sensory processing (e.g., Chanales et al., 2017; Favila et al., 2016; Zeithamova et al., 2018). At the same time, some studies have found differentiation effects in neocortex (e.g., Schlichting et al., 2015; Wammes et al., 2022). One possible explanation of these neocortical differentiation effects is that they are being ``propped up’’ by top-down feedback from differentiated representations in the hippocampus. This explanation implies that disruptions of hippocampal processing (e.g., lesions, stimulation) will eliminate these neocortical differentiation effects; we plan to test this prediction in future work.

Additionally, the simulations where we adjusted the oscillation amount (using our model of Schlichting et al., 2015) imply that differentiation will be most evident in brain regions where it is relatively hard to activate competitors. Given the U shape of the NMPH learning rule, limiting competitor activity makes it less likely that plasticity will ``cross over'' from weakening (and differentiation) to strengthening (and integration). Thus, within the hippocampus, subregions with sparser activity (e.g., dentate gyrus, and to a lesser extent, CA3; Barnes et al., 1990, GoodSmith et al., 2017; West et al., 1991) will be more prone to differentiation. There is strong empirical support for this prediction. For example, Wammes et al. (2022) manipulated the similarity of stimuli in a statistical learning experiment and found that moderate levels of visual similarity were associated with significant differentiation in the dentate gyrus but not other subregions. Also, numerous studies have found greater differentiation in dentate gyrus / CA3 than in CA1 (e.g., Dimsdale-Zucker et al., 2018; Wanjia et al., 2021; Molitor et al., 2021; Kim et al., 2017; but see Zheng et al., 2021).”

In the revised draft we have supplemented this discussion with a new section entitled “Reconciling the Prevalence of Differentiation in the Model and in the Data” (pp. 30-31):

“A key lesson from our model is that, from a computational perspective, it is challenging to obtain differentiation effects: The region of parameter space that gives rise to differentiation is much smaller than the one that gives rise to integration (for further discussion of this issue, see the section in Methods on Practical Advice for Getting the Model to Show Differentiation). However, the fact that integration is more prevalent in our simulations across parameter configurations does not mean that integration will be more prevalent than differentiation in real-life circumstances. What really matters in predicting the prevalence of differentiation in real life is how the parameters of the brain map on to parameters of the model: If the parameters of the brain align with regions of model parameter space that give rise to differentiation (even if these regions are small), this would explain why differentiation has been so robustly observed in extant studies. Indeed, this is exactly the case that we sought to make above about the hippocampus – i.e., that its use of especially sparse coding and a high learning rate will give rise to the kinds of neural dynamics that cause differentiation (as opposed to integration). As another example, while it is true that half of the overlap conditions in our simulation of Chanales et al. (2021) give rise to integration, this does not imply that integration will occur half of the time in the Chanales et al. (2021) study; it may be that the levels of overlap that are actually observed in the brain in Chanales et al. (2021) are more in line with the levels of overlap that give rise to differentiation in our model.”

(2) With real fMRI data we know that the actual correlation value doesn't matter all that much, and anti-correlations can be induced by things like preprocessing decisions. I am wondering if the important criterion in the model is that the correlations (e.g., as shown in Figure 6) go down from pre to post, versus that they are negative in sign during the post learning period. I would think that here, similar to in neural data, a decrease in correlation would be sufficient to conclude differentiation, but would love the authors' thoughts on that.

We thank the reviewer for bringing this up. In the paper, we define differentiation as the moving apart of representations – so we agree with the reviewer that it would be appropriate to conclude that differentiation is taking place when correlations go down from pre to post.

In addition to the definitional question (“what counts as differentiation”), one can also ask the mechanistic question of what is happening in the model at the (simulated) neuronal level in conditions where differentiation (i.e., an average decrease in similarity from pre to post) occurs. Here, the model’s answer is clear: When the similarity of two pairmates decreases, it is because the pairmates have acquired anticorrelated representations at the (simulated) neuronal level. When similarity decreases on average from pre to post, but the average “post” similarity value is not negative, this is because there is a mix of outcomes across runs of the model (due to variance in the initial, random model weights and also variance in the order in which items are presented across training epochs) – some runs lead to differentiation (manifested as anticorrelated pairmate representations) whereas others lead to no change or integration. The average pre-to-post change depends on the relative frequencies with which these different outcomes occur.

We have made several edits to the paper to clarify this point.

We added a new section under “Results” in our simulation of Chanales et al. (2021) entitled, “Pairs of Items that Differentiate Show Anticorrelated Representations” (p. 15):

“Figure 6B also highlights that, for learning rates where robust differentiation effects occur in aggregate (i.e., there is a reduction in mean pattern similarity, averaging across model runs), these aggregate effects involve a bimodal distribution across model runs: For some model runs, learning processes give rise to anticorrelated representations, and for other model runs the model shows integration; this variance across model runs is attributable to random differences in the initial weight configuration of the model. The aggregate differentiation effect is therefore a function of the proportion of model runs showing differentiation (here, anticorrelation) and the proportion of model runs showing integration. The fact that differentiation shows up as anticorrelation in the model's hidden layer relates to the learning effects discussed earlier:

Unique competitor units are sheared away from (formerly) shared units, so the competitor ends up not having any overlap with the target representation (i.e., the level of overlap is less than you would expect due to chance, which mathematically translates into anticorrelation). We return to this point and discuss how to test for anticorrelation in the Discussion section.”

We added new text to the “Take-Home Lessons” section in the Chanales et al. (2021) simulation (p. 17):

“In particular, the simulations expose some important boundary conditions for when representational change can occur according to the NMPH (e.g., that differentiation depends on a large learning rate, but integration does not), and the simulations provide a more nuanced account of exactly how representations change (e.g., that differentiation driven by the NMPH is always asymmetric, whereas integration is sometimes asymmetric and sometimes symmetric; and that, when differentiation occurs on a particular model run, it tends to give rise to anticorrelated representations in the model's hidden layer).”

We added new text to the “Nature of Representational Change” section in the Favila et al. (2016) simulation (p. 21):

“Figure 8 - Supplement 1 also indicates that, as in our simulation of Chanales et al. (2021), individual model runs where differentiation occurs show anticorrelation between the pairmate representations, and gradations in the aggregate level of differentiation that is observed across conditions reflect differences in the proportion of trials showing this anticorrelation effect.”

We added new text to the “Take-Home Lessons” section in the Favila et al. (2016) simulation (p.21):

“As in our simulation of \cite{chanales2021adaptive}, we found that the NMPH-mediated differentiation was asymmetric, manifested as anticorrelation between pairmate representations on individual model runs, and required a high learning rate, leading to abrupt representational change.”

We added new text to the “Nature of Representational Change” section in the Schlichting et al. (2015) simulation (p. 26):

“Also, as in our other simulations, when differentiation occurs on a particular model run it tends to give rise to anticorrelated representations (results not shown).”

We added new text to the “Take-Home Lessons” section in the Schlichting et al. (2015) simulation (pp. 26-27):

“As in the other versions of our model, differentiation requires a high learning rate, and – on model runs when it occurs – it is asymmetric and gives rise to anticorrelated representations.”

We added new text at the start of the Discussion (p. 27):

“In addition to qualitatively replicating the results from the studies we simulated, our model gives rise to several novel predictions – most notably, that differentiation driven by the NMPH requires a rapid learning rate and, when it occurs for a particular pair of items, it is asymmetric and gives rise to anticorrelated representations.”

We also added a new section in the Discussion entitled “Testing the Model's Prediction about Anticorrelation”, which (among other things) highlights the reviewer’s point that fMRI pattern similarity values can be affected by preprocessing choices (p. 30):

“Even though we operationally define differentiation as a reduction in similarity with learning, the way that it actually shows up on individual model runs is as anticorrelation between pairmates; in the model, the size of the aggregate differentiation effect is determined by the proportion of model runs that show this anticorrelation effect (vs. no change or integration). This implies that, if we could get a clean measurement of the similarity of pairmates in an experiment, we might see a multimodal distribution, with some pairmates showing anticorrelation, and others showing increased correlation (integration) or no change in similarity. This kind of clean readout of the similarity of individual pairs might be difficult to obtain with fMRI; it is more feasible that this could be obtained with electrophysiology. Another challenge with using fMRI to test this prediction is that anticorrelation at the individual-neuron level might not scale up to yield anticorrelation at the level of the BOLD response; also, fMRI pattern similarity values can be strongly affected by preprocessing choices – so a negative pattern similarity value does not necessarily reflect anticorrelation at the individual-neuron level. A final caveat is that, while we predict that differentiation will show up as anticorrelation in the brain region that gives rise to the differentiation effect, this might not translate into anticorrelation in areas that are downstream of this region (e.g., if the hippocampus is the source of the differentiation effect, we would expect anticorrelation there, but not necessarily in neocortical regions that receive input from the hippocampus; we revisit this point later in the discussion, when we address limitations and open questions).”

We added new text in the Discussion, under “Limitations and Open Questions” (p. 31):

“Importantly, while hippocampus can boost the representation of unique features in neocortex, we expect that neocortex will continue to represent shared perceptual features (e.g., in Favila et al., 2016, the fact that both pairmates are photos of barns). For this reason, in paradigms like the one used by Favila et al. (2016), the predicted effect of hippocampal differentiation on neocortical representations will be a reduction in pattern similarity (due to upregulation in the representation of unique pairmate features) but neocortex should not cross over into anticorrelation in these paradigms (due to its continued representation of shared perceptual features). Indeed, this is exactly the pattern that Wanjia et al. (2021) observed in their study, which used similar stimuli to those used in Favila et al. (2016).”

Lastly, we updated the Abstract (p. 1)

“What determines when neural representations of memories move together (integrate) or apart (differentiate)? Classic supervised learning models posit that, when two stimuli predict similar outcomes, their representations should integrate. However, these models have recently been challenged by studies showing that pairing two stimuli with a shared associate can sometimes cause differentiation, depending on the parameters of the study and the brain region being examined. Here, we provide a purely unsupervised neural network model that can explain these and other related findings. The model can exhibit integration or differentiation depending on the amount of activity allowed to spread to competitors – inactive memories are not modified, connections to moderately active competitors are weakened (leading to differentiation), and connections to highly active competitors are strengthened (leading to integration). The model also makes several novel predictions – most importantly, that when differentiation occurs as a result of this unsupervised learning mechanism, it will be rapid and asymmetric, and it will give rise to anticorrelated representations in the region of the brain that is the source of the differentiation. Overall, these modeling results provide a computational explanation for a diverse set of seemingly contradictory empirical findings in the memory literature, as well as new insights into the dynamics at play during learning.”

(3) For the modeling of the Favila et al. study, the authors state that a high learning rate is required for differentiation of the same-face pairs. This made me wonder what happens in the low learning rate simulations. Does integration occur?

For the same-face condition of the Favila simulation, lowering learning rate does not result in an overall integration effect:

Author response image 1.

In other cases, we do see integration emerge at lower learning rates – e.g., in the Schlichting interleaved condition we see a small integration effect emerge for a learning rate value of 0.3:

Author response image 2.

Our view is that, while integration can emerge at low learning rates, it is not a reliable property of the model – in some cases, there is a “window” of learning rates where there is enough learning to drive integration but not enough to drive differentiation, and in other cases there is not. Given this lack of reliability across simulations, we would prefer not to discuss this in the paper.

This paradigm has a lot of overlap with acquired equivalence, and so I am thinking about whether these are the sorts of small differences (e.g., same-category scenes and perhaps a high learning rate) that bias the system to differentiate instead of integrate.

We agree that it would be very interesting to use the model to explore acquired equivalence and related phenomena, but we think it is out of scope of the current paper. We have added some text to the Discussion under “Limitations and Open Questions” (p. 32):

“Another important future direction is to apply the model to a wider range of learning phenomena involving representational change – for example, acquired equivalence, which (like some of the studies modeled here) involves linking distinct stimuli to a shared associate (see, e.g., Honey and Hall, 1989; Shohamy and Wagner, 2008; Myers et al., 2003; Meeter et al., 2009; de Araujo Sanchez and Zeithamova, 2023). It is possible that some of these phenomena might be better explained by supervised learning, or a mixture of unsupervised and supervised learning, than by unsupervised learning alone.”

(4) For the simulations of the Schlichting et al. study, the A and B appear to have overlap in the hidden layer based on Figure 9, despite there being no similarity between the A and B items in the study (in contrast to Favila et al., in which they were similar kinds of scenes, and Chanales et al., in which they were similar colors). Why was this decision made? Do the effects depend on some overlap within the hidden layer? (This doesn't seem to be explained in the paper that I saw though, so maybe just it's a visualization error?)

Overlap in the pretrained hidden representations of A and B is not strictly necessary for these effects – it would be possible to reconfigure other parameters to get high levels of competition even if there were no overlap (e.g., by upregulating the strengths of connections from shared input features). Having said that, it is definitely true that overlap between the pretrained hidden representations boosts competition, and we think it is justified to posit this in the Schlichting simulation. We have now added an explanation for this in the paper (p. 23):

“New text in Schlichting, “Knowledge Built into the Network”

Matching the previous two simulations, we pretrained the weights so the hidden representations of the stimuli initially had 2/6 units in common. Even though the A and B stimuli used in the actual experiment did not have obvious feature overlap (they were randomly selected novel objects), it is important to note that the hidden layer is not simply a representation of the sensory features of the A and B stimuli; the hidden layer also receives input from the output layer, which represents the shared associate of A and B (X). We think that the presence of this shared associate justifies our use of initially-overlapping hidden representations.”

(5) It seems as though there were no conditions under which the simulations produced differentiation in both the blocked and intermixed conditions, which Schlichting et al. observed in many regions (as the present authors note). Is there any way to reconcile this difference?

We thank the reviewer for bringing this up. If we set the connection strength between X (in the output layer) and A (in the hidden layer) in the blocked condition to .9 instead of .999 (keeping this connection strength at .8 for the interleaved condition) and we set Osc to .0615, we observe differentiation in both conditions.

Rather than replacing the original results in the paper, which would entail re-making the associated videos, etc., we have added a supplementary figure (Figure 10 - Supplement 1), which is included on p. 46.

We also added the following to the Results section of the Schlichting simulation in the main text (p. 26):

“Figure 10 - Supplement 1 shows results from an alternative parameterization where, in the low-oscillation-amplitude condition, differentiation is observed in both the blocked and interleaved conditions (mirroring results from Schlichting et al., 2015, who found differentiation in both conditions in several regions of interest, including parts of the hippocampus and medial prefrontal cortex).”

(6) A general question about differentiation/repulsion and how it affects the hidden layer representation in the model: Is it the case that the representation is actually "shifted" or repelled over so it is no longer overlapping? Or do the shared connections just get pruned, such that the item that has more "movement" in representational space is represented by fewer units on the hidden layer (i.e., is reduced in size)? I think, if I understand correctly, that whether it gets shifted vs. reduce would depend on the strength of connections along the hidden layer, which would in turn depend on whether it represents some meaningful continuous dimension (like color) or not. But, if the connections within the hidden layer are relatively weak and it is the case that representations become reduced in size, would there be any anticipated consequences of this (e.g., cognitively/behaviorally)?

The representations are shifted – this is discussed in the Chanales results section:

“Because the activity ``set point'' for the hidden layer (determined by the kWTA algorithm) involves having 6 units active, and the unique parts of the competitor only take up 4 of these 6 units, this leaves room for activity to spread to additional units. Given the topographic projections in the output layer, the model is biased to ``pick up'' units that are adjacent in color space to the currently active units; because activity cannot flow easily from the competitor back to the target (as a result of the aforementioned severing of connections), it flows instead {\em away} from the target, activating two additional units, which are then incorporated into the competitor representation. This sequence of events (first a severing of the shared units, then a shift away from the target) completes the process of neural differentiation, and is what leads to the behavioral repulsion effect in color recall (because the center-of-mass of the color representation has now shifted away from the target).”

Reviewer #2 (Public Review):

This paper addresses an important computational problem in learning and memory. Why do related memory representations sometimes become more similar to each other (integration) and sometimes more distinct (differentiation)? Classic supervised learning models predict that shared associations should cause memories to integrate, but these models have recently been challenged by empirical data showing that shared associations can sometimes cause differentiation. The authors have previously proposed that unsupervised learning may account for these unintuitive data. Here, they follow up on this idea by actually implementing an unsupervised neural network model that updates the connections between memories based on the amount of coactivity between them. The goal of the authors' paper is to assess whether such a model can account for recent empirical data at odds with supervised learning accounts. For each empirical finding they wish to explain, the authors built a neural network model with a very simple architecture (two inputs layers, one hidden layer, and one output layer) and with prewired stimulus representations and associations. On each trial, a stimulus is presented to the model, and inhibitory oscillations allow competing memories to pop up. Pre-specified u-shaped learning rules are used to update the weights in the model, such that low coactivity leaves model connections unchanged, moderate coactivity weakens connections, and high coactivity strengthens connections. In each of the three models, the authors manipulate stimulus similarity (following Chanales et al), shared vs distinct associations (following Favila et al), or learning strength (a stand in for blocked versus interleaved learning schedule; following Schlichting et al) and evaluate how the model representations evolve over trials.

As a proof of principle, the authors succeed in demonstrating that unsupervised learning with a

simple u-shaped rule can produce qualitative results in line with the empirical reports. For instance, they show that pairing two stimuli with a common associate (as in Favila et al) can lead to *differentiation* of the model representations. Demonstrating these effects isn't trivial and a formal modeling framework for doing so is a valuable contribution. Overall, the authors do a good job of both formally describing their model and giving readers a high level sense of how their critical model components work, though there are some places where the robustness of the model to different parameter choices is unclear. In some cases, the authors are very clear about this (e.g. the fast learning rate required to observe differentiation). However, in other instances, the paper would be strengthened by a clearer reporting of the critical parameter ranges.

We thank the reviewer for raising this point. The interdependence of parameters in our model makes it infeasible to identify critical parameter ranges. We have added a paragraph to the “Approach to Parameterization and Data Fitting” section in the Methods to address this point (p. 33):

“The overall goal of this modeling work is to account for key empirical regularities regarding differentiation and integration and to establish boundary conditions on these regularities. As such, the modeling work described below focuses more on qualitative fits to general properties of the data space than on quantitative fits to results from specific studies. Automatic parameter optimization is not feasible for this kind of model, given the large number of model parameters and the highly interactive, nonlinear nature of competitive dynamics in the model; consequently, model fitting was done by hand.

These complex interactions between parameters also make it infeasible to list “critical parameter ranges” for generating particular model outcomes. Our experience in working with the model has been that activation dynamics are what matter most for learning, and that disparate parameter sets can give rise to the same activation dynamics and -- through this -- the same learning effects; likewise, similar parameter sets can give rise to different activation dynamics and different learning outcomes. Consequently, in this paper we have focused on characterizing the dynamics that give rise to different learning effects (and how they can be affected by local parameter perturbations, e.g., relating to learning rate and oscillation size), rather than the – impossible, we believe – task of enumerating the full set of parameter configurations that give rise to a particular result.”

For instance, it's clear from the manipulation of oscillation strength in the model of Schlichting et al that this parameter can dramatically change the direction of the results. The authors do report the oscillation strength parameter values that they used in the other two models, but it is not clear how sensitive these models are to small changes in this value.

In some cases, the effects of oscillation strength are relatively smooth. For example, in the Favila simulation, increasing the oscillation amplitude Osc effectively recapitulates the U-shaped curve (i.e., higher levels of Osc lead to more competitor activation, which initially leads to weakening / differentiation but then gives way to strengthening / integration), as is shown for the Favila Different Face condition in this plot:

Author response image 3.

In the Chanales 2/6 overlap condition, the effects of varying Osc are more nonlinear:

Author response image 4.

We think this is attributable to the increased “all-or-none” recurrent dynamics in this simulation (due to the recurrent projections within the output layer), which make it more difficult to evoke moderate (vs. high) levels of activation. This difficulty in reliably obtaining graded activation dynamics is likely a consequence of the small-scale (“toy”) nature of the model and the simple inhibitory mechanisms employed here, as opposed to being a generalizable property of the brain – presumably, the actual brain employs more nuanced and effective means of controlling activation. Furthermore, we don’t think that the high prevalence of integration in the model’s parameter space necessarily translates into a prediction that integration should be more prevalent overall – see the new “Reconciling the Prevalence of Differentiation in the Model and in the Data” section described in response to one of the reviewer’s other points below. Due to the paper already being quite long, we have opted not to include the above plots / discussion in the paper.

Similarly, it's not clear whether the 2/6 hidden layer overlap (only explicitly manipulated in the model of Chanales et al) is required for the other two models to work.

When we were parameterizing the model, we opted to keep the 2/6 level of overlap for all of the simulations and we adjusted other parameters to fit the data; in part, this was because overlap can only be adjusted in discrete jumps, whereas other influential parameters in the model can be adjusted in a more graded, real-valued way. Our use of 2/6 overlap (as opposed to, say, 1/6 or 3/6 overlap) for the Favila and Schlichting models was done out of convenience, and should not be interpreted as a strong statement that this particular level of overlap is necessary for obtaining differentiation; we could easily get the model to show differentiation given other overlap levels by adjusting other parameters.

Finally, though the u-shaped learning rule is essential to this framework, the paper does little formal investigation of this learning rule. It seems obvious that allowing the u-shape to collapse too much toward a horizontal line would reduce the model's ability to account for empirical results, but there may be other more interesting features of the learning rule parameterization that are essential for the model to function properly.

Given that the paper is already quite long, we have opted not to include further exploration of the parameters of the U-shaped learning rule in the paper. However, for the reviewer’s information, we report the effects of a few illustrative manipulations of these parameters below. As a general principle, the effects of these manipulations make sense in light of the theoretical framework described in the paper.

For example, the parameter “DRevMag” controls the size of the negative “dip” in the U-shaped curve (more negative values = a larger dip). Given that this negative dip is essential for severing weights to competitors and causing differentiation, shifting DRevMag upwards towards zero should shift the balance of the model away from differentiation and towards integration. This is indeed what we observe, as shown in this parameter sweep from the Chanales simulation:

Author response image 5.

As another example: The “DRev” parameter controls where the U-shaped curve transitions from negative weight change to positive weight change. Lower values of DRev mean that the region of coactivity values leading to negative weight change will be smaller, and the region of coactivity values leading to positive weight change will be larger. As such, we would expect that lower values of DRev would bias the model toward integration. That is indeed the case, as shown in this parameter sweep from the Schlichting Blocked simulation:

Author response image 6.

There are a few other points that may limit the model's ability to clearly map onto or make predictions about empirical data. The model(s) seems very keen to integrate and do so more completely than the available empirical data suggest. For instance, there is a complete collapse of representations in half of the simulations in the Chanales et al model and the blocked simulation in the Schlichting et al model also seems to produce nearly complete integration Even if the Chanales et al paper had observed some modest behavioral attraction effects, this model would seem to over-predict integration. The author's somewhat implicitly acknowledge this when they discuss the difficulty of producing differentiation ("Practical Advice for Getting the Model to Show Differentiation") and not of producing integration, but don't address it head on.

We thank the reviewer for this comment – R1 had a similar comment. We have added a new section to the Discussion to address this point (p. 30):

“Reconciling the Prevalence of Differentiation in the Model and in the Data.

A key lesson from our model is that, from a computational perspective, it is challenging to obtain differentiation effects: The region of parameter space that gives rise to differentiation is much smaller than the one that gives rise to integration (for further discussion of this issue, see the section in Methods on Practical Advice for Getting the Model to Show Differentiation). However, the fact that integration is more prevalent in our simulations across parameter configurations does not mean that integration will be more prevalent than differentiation in real-life circumstances. What really matters in predicting the prevalence of differentiation in real life is how the parameters of the brain map on to parameters of the model: If the parameters of the brain align with regions of model parameter space that give rise to differentiation (even if these regions are small), this would explain why differentiation has been so robustly observed in extant studies. Indeed, this is exactly the case that we sought to make above about the hippocampus – i.e., that its use of especially sparse coding and a high learning rate will give rise to the kinds of neural dynamics that cause differentiation (as opposed to integration). As another example, while it is true that half of the overlap conditions in our simulation of Chanales et al. (2021) give rise to integration, this does not imply that integration will occur half of the time in the Chanales et al. (2021) study; it may be that the levels of overlap that are actually observed in the brain in Chanales et al. (2021) are more in line with the levels of overlap that give rise to differentiation in our model.”

Second, the authors choice of strongly prewiring associations in the Chanales and Favila models makes it difficult to think about how their model maps onto experimental contexts where competition is presumably occurring while associations are only weakly learned. In the Chanales et al paper, for example, the object-face associations are not well learned in initial rounds of the color memory test. While the authors do justify their modeling choice and their reasons have merit, the manipulation of AX association strength in the Schlichting et al model also makes it clear that the association strength has a substantial effect on the model output. Given the effect of this manipulation, more clarity around this assumption for the other two models is needed.

We thank the reviewer for bringing this up. We have edited the section entitled “A Note on Prewiring Representations” in the Methods to further justify our choice to prewire associations in the Chanales and Favila models (p. 37):

“In our model, our practice of ``prewiring'' memory representations for the A and B pairmates serves two functions. In some cases, it is meant to stand in for actual training (as in the blocked / interleaved manipulation; the connections supporting the AX association are prewired to be stronger in the blocked condition than in the interleaved condition). However, the other, more fundamental role of prewiring is to ensure that the A and B input patterns evoke sparse distributed representations in the hidden layer (i.e., where some units are strongly active but most other units are inactive). In the real brain, this happens automatically because the weight landscape has been extensively sculpted by both experience and evolution. For example, in the real hippocampus, when the second pairmate is presented for the first time, it will evoke a sparse distributed representation in the CA3 subfield (potentially overlapping with the first pairmate’s CA3 representation) even before any learning of the second pairmate has occurred, due to the strong, sparse mossy fiber projections that connect the dentate gyrus to CA3 (McNaughton & Morris, 1987). As discussed above, we hypothesize that this initial, partial overlap between the second pairmate’s representation and the first pairmate’s representation can lead to pop-up of the unique features of the first pairmate’s representation, triggering learning that leads to differentiation or integration. In our small-scale model, we are effectively starting with a ``blank brain''; in the absence of prewiring, the A and B inputs would activate overly diffuse representations that do not support these kinds of competitive dynamics. As such, prewiring in our model is necessary for proper functioning. The presence of prewired A and B representations should therefore not be interpreted as reflecting a particular training history (except in the blocked / interleaved case above); rather, these prewired representations constitute the minimum step we would take to ensure well-defined competitive dynamics in our small-scale model.

The fact that connection strengths serve this dual function – sometimes reflecting effects of training (as in our simulation of Schlichting et al., 2015) and in other cases reflecting necessary prewiring – complicates the interpretation of these strength values in the model. Our view is that this is a necessary limitation of our simplified modeling approach – one that can eventually be surmounted through the use of more biologically-detailed architectures (see Limitations and Open Questions in the Discussion).”

Overall, this is strong and clearly described work that is likely to have a positive impact on computational and empirical work in learning and memory. While the authors have written about some of the ideas discussed in this paper previously, a fully implemented and openly available model is a clear advance that will benefit the field. It is not easy to translate a high-level description of a learning rule into a model that actually runs and behaves as expected. The fact that the authors have made all their code available makes it likely that other researchers will extend the model in numerous interesting ways, many of which the authors have discussed and highlighted in their paper.

Reviewer #3 (Public Review):

This paper proposes a computational account for the phenomenon of pattern differentiation (i.e., items having distinct neural representations when they are similar). The computational model relies on a learning mechanism of the nonmonotonic plasticity hypothesis, fast learning rate and inhibitory oscillations. The relatively simple architecture of the model makes its dynamics accessible to the human mind. Furthermore, using similar model parameters, this model produces simulated data consistent with empirical data of pattern differentiation. The authors also provide insightful discussion on the factors contributing to differentiation as opposed to integration. The authors may consider the following to further strengthen this paper:

The model compares different levels of overlap at the hidden layer and reveals that partial overlap seems necessary to lead to differentiation. While I understand this approach from the perspective of modeling, I have concerns about whether this is how the human brain achieves differentiation. Specifically, if we view the hidden layer activation as a conjunctive representation of a pair that is the outcome of encoding, differentiation should precede the formation of the hidden layer activation pattern of the second pairmate. Instead, the model assumes such pattern already exists before differentiation. Maybe the authors indeed argue that mechanistically differentiation follows initial encoding that does not consider similarity with other memory traces?

Related to the point above, because the simulation setup is different from how differentiation actually occurs, I wonder how valid the prediction of asymmetric reconfiguration of hidden layer connectivity pattern is.

We thank the reviewer for this comment. In the revised manuscript, we have edited the “Note on Prewiring Representations” in the Methods to clarify how our assumptions about prewiring relate to what we really think is happening in the brain (p. 37):

“In our model, our practice of ``prewiring'' memory representations for the A and B pairmates serves two functions. In some cases, it is meant to stand in for actual training (as in the blocked / interleaved manipulation; the connections supporting the AX association are prewired to be stronger in the blocked condition than in the interleaved condition). However, the other, more fundamental role of prewiring is to ensure that the A and B input patterns evoke sparse distributed representations in the hidden layer (i.e., where some units are strongly active but most other units are inactive). In the real brain, this happens automatically because the weight landscape has been extensively sculpted by both experience and evolution. For example, in the real hippocampus, when the second pairmate is presented for the first time, it will evoke a sparse distributed representation in the CA3 subfield (potentially overlapping with the first pairmate’s CA3 representation) even before any learning of the second pairmate has occurred, due to the strong, sparse mossy fiber projections that connect the dentate gyrus to CA3 (McNaughton & Morris, 1987). As discussed above, we hypothesize that this initial, partial overlap between the second pairmate’s representation and the first pairmate’s representation can lead to pop-up of the unique features of the first pairmate’s representation, triggering learning that leads to differentiation or integration. In our small-scale model, we are effectively starting with a ``blank brain''; in the absence of prewiring, the A and B inputs would activate overly diffuse representations that do not support these kinds of competitive dynamics. As such, prewiring in our model is necessary for proper functioning. The presence of prewired A and B representations should therefore not be interpreted as reflecting a particular training history (except in the blocked / interleaved case above); rather, these prewired representations constitute the minimum step we would take to ensure well-defined competitive dynamics in our small-scale model.

The fact that connection strengths serve this dual function – sometimes reflecting effects of training (as in our simulation of Schlichting et al., 2015) and in other cases reflecting necessary prewiring – complicates the interpretation of these strength values in the model. Our view is that this is a necessary limitation of our simplified modeling approach – one that can eventually be surmounted through the use of more biologically-detailed architectures (see Limitations and Open Questions in the Discussion).”

Although as the authors mentioned, there haven't been formal empirical tests of the relationship between learning speed and differentiation/integration, I am also wondering to what degree the prediction of fast learning being necessary for differentiation is consistent with current data. According to Figure 6, the learning rates lead to differentiation in the 2/6 condition achieved differentiation after just one-shot most of the time. On the other hand, For example, Guo et al (2021) showed that humans may need a few blocks of training and test to start showing differentiation.

We thank the reviewer for mentioning this. We have added a paragraph to the “Differentiation Requires a High Learning Rate and Is Sensitive to Activity Dynamics” section of the Discussion that addresses this point (pp. 28-29):

“Although the results from Wanjia et al. (2021) provide strong support for the model's prediction that differentiation will be abrupt, they raise another question: What explains variance across items in when this abrupt change takes place? The answer to this question remains to be seen, but one possibility is encoding variability: If we assume that participants stochastically sample (i.e., attend to) the features of the scene pairmates, it is possible that participants might initially fail to sample the features that distinguish the scene pairmates, which can be quite subtle – and if the distinguishing features of the pairmates are not represented in high-level visual regions (i.e., the pairmates are represented in these regions as having the same features), this could delay the onset of differentiation until the point at which the distinguishing features happen (by chance) to be sampled.”

Related to the point above, the high learning rate prediction also seems to be at odds with the finding that the cortex, which has slow learning (according to the theory of complementary learning systems), also shows differentiation in Wammes et al (2022).

We now address this point in the section of the Discussion entitled “Differentiation Requires a High Learning Rate and Is Sensitive to Activity Dynamics” (p. 27):

“Our finding that differentiation requires a high learning rate suggests that differentiation will be more evident in the hippocampus than in neocortex, insofar as hippocampus is thought to have a higher learning rate than neocortex (McClelland et al., 1995). In keeping with this prediction, numerous studies have found differentiation effects in hippocampus but not in neocortical regions involved in sensory processing (e.g., Chanales et al., 2017; Favila et al., 2016; Zeithamova et al., 2018). At the same time, some studies have found differentiation effects in neocortex (e.g., Schlichting et al., 2015; Wammes et al., 2022). One possible explanation of these neocortical differentiation effects is that they are being ``propped up’’ by top-down feedback from differentiated representations in the hippocampus.”

More details about the learning dynamics would be helpful. For example, equation(s) showing how activation, learning rate and the NMPH function work together to change the weight of connections may be added. Without the information, it is unclear how each connection changes its value after each time point.

We thank the reviewer for this comment. We have made two major changes to address this concern. First, we have edited the “Learning” section within “Basic Network Properties” in the main text (pp. 6-7):

“Connection strengths in the model between pairs of connected units x and y were adjusted at the end of each trial (i.e., after each stimulus presentation) as a U-shaped function of the coactivity of x and y, defined as the product of their activations on that trial. The parameters of the U-shaped learning function relating coactivity to change in connection strength (i.e., weakening / strengthening) were specified differently for each projection where learning occurs (bidirectionally between the input and hidden layers, the hidden layer to itself, and the hidden to output layer). Once the U-shaped learning function for each projection in each version of the model was specified, we did not change it for any of the various conditions. Details of how we computed coactivity and how we specified the U-shaped function can be found in the Methods section.”

Second, we have added the requested equations to the “Learning” part of the Methods (pp. 37-38):

The right side of the function, strong activation leads to strengthening of the connectivity, which I assume will lead to stronger activation on the next time point. The model has an upper limit of connection strength to prevent connection from strengthening too much. The same idea can be applied to the left side of the function: instead of having two turning points, it can be a linear function such that low activation keeps weakening connection until the lower limit is reached. This way the NMPH function can take a simpler form (e.g., two line-segments if you think the weakening and strengthening take different rates) and may still simulate the data.

We thank the reviewer for mentioning this. We have added a new paragraph in the “Learning” section of the Methods to justify the particular shape of the learning curve (pp. 38-39):

“Evidence for the U-shaped plasticity function used here (where low activation leads to no change, moderate activation leads to weakening, and higher levels of activation lead to strengthening) was previously reviewed in Ritvo et al. (2019). In brief, there are three lines of work that support the U shape: First, multiple neurophysiological studies have found that moderate postsynaptic depolarization leads to synaptic weakening and higher levels of depolarization lead to synaptic strengthening (e.g., Artola et al., 1990; Hansel et al., 1996). Second, human neuroscience studies have used pattern classifiers, applied to fMRI and EEG data, to measure memory activation, and have related this measure to subsequent memory accessibility; several studies using this approach have found that low levels of activation lead to no change in memory strength, moderate levels of activation lead to impaired subsequent memory, and higher levels of activation lead to increased subsequent memory (e.g., Newman and Norman, 2010; Detre et al., 2013; Kim et al., 2014; for related findings, see Lewis-Peacock and Norman, 2014; Wang et al., 2019). Third, a recent human fMRI study by Wammes et al. (2022) manipulated memory activation by varying the visual similarity of pairmates and observed a U-shaped function relating visual similarity to representational change in the hippocampus, whereby low levels of pairmate similarity were associated with no change, moderate levels of similarity were associated with differentiation, and the differentiation effect went away at higher levels of similarity.

We have also included a pointer to this new paragraph in the “Nonmonotonic Plasticity Hypothesis” section of Introduction (p. 2):

(for further discussion of the empirical justification for the NMPH, see the Learning subsection in the Methods)”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

A few additional minor things about data presentation and the like:

(1) Figure 1 legend - a more general description of how to interpret the figure might be helpful for more naive readers (e.g., explaining how one can visualize in the schematic that there is overlap in the hidden layer between A and B). Also, from the Figure 1 depiction, it's not clear what is different about the setup from the initial left hand side panels in A, B, C, to make it such that activity spreads strongly to A in panel A, weakly in panel B, and not at all in panel C since the weights are the same. Is there a way to incorporate this into the graphic, or describe it in words?

To address this point, we have added the following text to the Figure 1 caption (p. 3):

“Note that the figure illustrates the consequences of differences in competitor activation for learning, without explaining why these differences would arise. For discussion of circumstances that could lead to varying levels of competitor activation, see the simulations described in the text.”

(2) I believe not all of the papers cited on lines 193-195 actually have similarity manipulations in them. I'd recommend double checking this list and removing those less relevant to the statement.

Thank you for pointing this out; we have removed the Ballard reference and we have clarified what we mean by similarity reversal (p. 7):

“The study was inspired by recent neuroimaging studies showing ``similarity reversals'', wherein stimuli that have more features in common (or share a common associate) show less hippocampal pattern similarity (Favila et al., 2016; Schlichting et al., 2015; Molitor et al., 2021; Chanales et al., 2017; Dimsdale-Zucker et al., 2018; Wanjia et al., 2021; Zeithamova et al., 2018; Jiang et al., 2020; Wammes et al., 2022).”

(3) I wanted a bit more detail about how the parameters were set in the main paper, not just in the methods. Even something as brief as noting that model fitting was done by hand by tweaking parameters to re-create the empirical patterns (if I'm understanding correctly) would have been helpful for me.

To address this point, we have added the following text under “Basic Network Properties” (p. 4):

“Our goal was to qualitatively fit key patterns of results from each of the aforementioned studies. We fit the parameters of the model by hand as they are highly interdependent (see the Methods section for more details).”

(4) In Figure 4E, it would be helpful to describe the x and y axes of the MDS plots in the legend.

To address this point, we have added the following new text to the Figure 4 caption that clarifies how the MDS plots were generated (p. 11):

“MDS plots were rotated, shifted, and scaled such that pairmate 1before is located at (0,0), pairmate 2before is located directly to the right of pairmate 1before, and the distance between pairmate 1before and pairmate 2before is proportional to the baseline distance between the pairmates.”

(5) Figure 6 - at first I thought the thicker line was some sort of baseline, but I think it is just many traces on top of one another. If other readers may be similarly confused, perhaps this could be stated.

Thanks for this comment. We have updated Figure 6 (p. 16).

We have also updated the caption.

I am having a lot of difficulty understanding the terms "competitor-to-competitor,"

"competitor-to-target/shared," and "target/shared-to-target/shared," and therefore I don't fully get Figure 5. I think it might be helpful to expand the description of these terms where they are first introduced in the paper (p. 13?). I think I am missing something crucial here, and I am not quite sure what that is-which I know is not very helpful! But, to narrate my confusion a bit, I thought that these terms would somehow relate to connections between different connections of the network. For example is competitor-to-competitor within the hidden layer? Or is this somehow combining across relevant connections that might span different pairs of layers in the model? And, I really have no idea why it is "target/shared."

Thank you for these comments. We have updated Figure 5 and we have also made several changes to the main text and the figure caption to address these points.

Changes to the main text (p. 13):

“Whether symmetric or asymmetric integration occurs depends on the relative strengths of connections between pairs of unique competitor units (competitor-competitor connections) compared to connections between unique competitor units and shared units (competitor-shared connections) after the first trial (Figure 5; note that the figure focuses on connections between hidden units, but the principle also applies to connections that span across layers). Generally, coactivity between unique competitor units (competitor-competitor coactivity) is less than coactivity between unique competitor units and shared units (competitor-shared coactivity), which is less than coactivity between unique target units and shared units (target-shared coactivity).”

(7) Relatedly in Figure 13, I understand how some competitor-to-target/shared connections could be spared in the bottom instance given panel B. However, I'm struggling to understand how that relates to the values in the corresponding chart in panel A. What about panel A, bottom (vs. the top) means lower coactivities between some competitor-to-target/shared? Is it because if the noise level is higher, the "true" activation of competitor-to-target/shared connections is weaker? I think again, I'm missing something critical here! and wonder if other readers may be in the same situation. (I know the authors described this also on p. 36, but I'm still confused!)

We have updated Figure 13 to clarify these points.

(8)  In Figure 9, I believe there is no caption for panel D. Also, it looks as though the item unit active for A and B is the same. I wonder if this is an error?

Thank you for catching these errors! They have both been fixed.

Reviewer #2 (Recommendations For The Authors):

-Perhaps I missed it, but I think defining coactivity (how it is computed) in the main text would be useful for readers, as this is critical for understanding the model. I did find it in the methods.

We thank the reviewer for this suggestion. We have updated the “Learning” section within “Basic Network Properties” in the main text to address this point (pp. 6-7):

“Connection strengths in the model between pairs of connected units x and y were adjusted at the end of each trial (i.e., after each stimulus presentation) as a U-shaped function of the coactivity of x and y, defined as the product of their activations on that trial. The parameters of the U-shaped learning function relating coactivity to change in connection strength (i.e., weakening / strengthening) were specified differently for each projection where learning occurs (bidirectionally between the input and hidden layers, the hidden layer to itself, and the hidden to output layer). Once the U-shaped learning function for each projection in each version of the model was specified, we did not change it for any of the various conditions. Details of how we computed coactivity and how we specified the U-shaped function can be found in the Methods section.”

-The modeling results in the different face condition are at odds with the data for the Favila et al model (they observe some differentiation in the paper and the model predicts no change). This could be due to a number of unmodeled factors, but it is perhaps worth noting.

Thank you for pointing this out. It is possible to better capture the pattern of results observed by Favila et al. in their paper (with some differentiation in the different-face condition and even more differentiation in the same-face condition) by slightly adjusting the model parameters (specifically, by setting the oscillation amplitude Osc for the hidden layer to .1 instead of .067).

Rather than replacing the old (Osc \= .067) results in the paper, which would entail re-making the associated videos, etc., we have added a supplementary figure (Figure 8 - Supplement 1; see p.45):

We also added new text to the Favila Results, under “Differentiation and Integration” (p. 20):

“Note also that the exact levels of differentiation that are observed in the different-face and same-face conditions are parameter dependent; for an alternative set of results showing some differentiation in the different-face condition (but still less than is observed in the same-face condition), see Figure 8 - Supplement 1.”

-Related to my comment in the public review about pre-wiring associations, in the caption for Figure 9 (Schlichting model), the authors report "In both conditions, the pre-wired connection linking the "item B" hidden units to the "item X" output unit is set to .7. In the interleaved condition, the connection linking the "item A" hidden units to the "item X" output unit is set to .8, to reflect some amount of initial AX learning. In the blocked condition, the connection linking the "item A" hidden units to the "item X" output unit is set a higher value (.999), to reflect extra AX learning." What are the equivalent values for the other models, especially the Favila model since the structure is the same as Schlichting? I understood all the "strong" connections to be .99 unless otherwise stated. If that's the case, I don't understand why the blocked Schlichting model and the Favila model produce opposite effects. More clarity would be useful here.

We have added a new paragraph to the results section for the Schlicting model (under “Differentiation and Integration”) to clarify why the blocked Schlichting model and the Favila model show different results (p. 24):

“Note that the key feature driving integration in the blocked condition of this simulation is not the high strength of the connection from X to A on its own – rather, it is the asymmetry in the pretrained connection strengths from X to A (.999) and from X to B (.7). This asymmetry, which is meant to reflect the extensive training on A-X that occurred before the initial presentation of B-X, results in the A-X hidden representation decisively winning the competition during B-X presentation, which then leads to the B input also being linked to this representation (i.e., integration). It is instructive to compare this to the same-face condition from our simulation of Favila et al. (2016): In that simulation, the two pairmates are also linked strongly (.99 initial connection strength) to a shared associate, but in that case the connections are equally strong, so there is more balanced competition -- in this case, the competitor representation only comes to mind moderately (instead of displacing the target representation), so the result is differentiation instead of integration.”

-The meaning of the different colored dots in Figure 5 is bit hard to keep track of, even given the legend labels. The figure might benefit from a model sketch highlighting each of the different coactivity types. The left side of Fig 13 was useful but again somehow mapping on the colors would help further. Another note on these figures: what does having two dots of each color mean? Is it just an illustration of the variance? There would be more dots if there was one dot per coactivity value.

We have updated Figure 5 and Figure 13 to clarify these points (including a clarification that the dots only represent a subset of the possible pairings between units).

-While I appreciate the goal of the paper is to account for these three studies, readers who aren't familiar with or specifically interested in these studies may appreciate a small amount of intuition on why formalizing unsupervised learning models may be broadly important for computational investigations of learning/memory/cognition.

We have added the following text under “Basic Network Properties” in the Introduction to address this point (p. 4):

“Achieving a better understanding of unsupervised learning is an important goal for computational neuroscience, given that learning agents have vastly more opportunities to learn in an unsupervised fashion than from direct supervision (for additional discussion of this point, see, e.g., Zhuang et al., 2021).”

Author response:

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

eLife assessment

In this useful study, the authors report the efficacy, hematological effects, and inflammatory response of the BPaL regimen (containing bedaquiline, pretomanid, and linezolid) compared to a variation in which Linezolid is replaced with the preclinical development candidate spectinamide 1599, administered by inhalation in tuberculosis-infected mice. The authors provide convincing evidence that supports the replacement of Linezolid in the current standard of care for drug-resistant tuberculosis. However, a limitation of the work is the lack of control experiments with bedaquiline and pretomanid only, to further dissect the relevant contributions of linezolid and spectinamide in efficacy and adverse effects.

We acknowledge a limitation in our study due to lack of groups with monotherapy of bedaquiline and pretomanid however, similar studies to understand contribution of bedaquiline and pretomanid to the BPaL have been published already (references #4 and #60 in revised manuscript).  Our goal was to compare the BPaS versus the BPaL with the understanding that TB treatment requires multidrug therapy.   We omitted monotherapy groups to reduce complexity of the studies because the multidrug groups require very large number of animals with very intensive and complex dosing schedules. Even if B or Pa by themselves have better efficacy than the BPa or BPaL combination, patients will not be treated with only B or Pa because of very high risk of developing drug resistance to B or/and PA. If drug resistance is developed for B or Pa, the field will lose very effective drugs against TB. 

Although the manuscript is well written overall, a re-formulation of some of the stated hypotheses and conclusions, as well as the addition of text to contextualize translatability, would improve value.

Manuscript has been edited to address these critiques.  Answers to individual critiques are below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript is an extension of previous studies by this group looking at the new drug spectinamide 1599. The authors directly compare therapy with BPaL (bedaquiline, pretomanid, linezolid) to a therapy that substitutes spectinamide for linezolid (BPaS). The Spectinamide is given by aerosol exposure and the BPaS therapy is shown to be as effective as BPaL without adverse effects. The work is rigorously performed and analyses of the immune responses are consistent with curative therapy.

Strengths:

(1) This group uses 2 different mouse models to show the effectiveness of the BPaS treatment.

(2) Impressively the group demonstrates immunological correlates associated with Mtb cure with the BPaS therapy.

(3) Linezolid is known to inhibit ribosomes and mitochondria whereas spectinaminde does not. The authors clearly demonstrate the lack of adverse effects of BPaS compared to BPaL.

Weaknesses:

(1) Although this is not a weakness of this paper, a sentence describing how the spectinamide would be administered by aerosolization in humans would be welcomed.

We already reported on the aerodynamic properties of dry powder spectinamide 1599 within #3 HPMC capsules and its delivery from a RS01 Plastiape inhaler device (reference #59 in revised manuscript).  To address this critique, we added a last paragraph in discussion “It is proposed that human use of spectinamides 1599 will be administered using a dry powder formulation delivered by the RS01 Plastiape dry powder inhaler" (reference #59 in revised manuscript).  

Reviewer #2 (Public Review):

Summary:

Replacing linezolid (L) with the preclinical development candidate spectinamide 1599, administered by inhalation, in the BPaL standard of care regimen achieves similar efficacy, and reduces hematological changes and proinflammatory responses.

Strengths:

The authors not only measure efficacy but also quantify histological changes, hematological responses, and immune responses, to provide a comprehensive picture of treatment response and the benefits of the L to S substitution.

The authors generate all data in two mouse models of TB infection, each reproducing different aspects of human histopathology.

Extensive supplementary figures ensure transparency. 

Weaknesses:

The articulation of objectives and hypotheses could be improved.

We edited to "The AEs were associated with the long-term administration of the protein synthesis inhibitor linezolid. Spectinamide 1599 (S) is also a protein synthesis inhibitor of Mycobacterium tuberculosis with an excellent safety profile, but which lacks oral bioavailability. Here, we propose to replace L in the BPaL regimen with spectinamide administered via inhalation and we demonstrate that inhaled spectinamide 1599, combined with BPa ––BPaS regimen––has similar efficacy to that of BPaL regimen while simultaneously avoiding the L-associated AEs.

Reviewer #3 (Public Review):

Summary:

In this paper, the authors sought to evaluate whether the novel TB drug candidate, spectinamide 1599 (S), given via inhalation to mouse TB models, and combined with the drugs B (bedaquiline) and Pa (pretomanid), would demonstrate similar efficacy to that of BPaL regimen (where L is linezolid). Because L is associated with adverse events when given to patients long-term, and one of those is associated with myelosuppression (bone marrow toxicity) the authors also sought to assess blood parameters, effects on bone marrow, immune parameters/cell effects following treatment of mice with BPaS and BPaL. They conclude that BPaL and BPaS have equivalent efficacy in both TB models used and that BPaL resulted in weight loss and anemia (whereas BPaL did not) under the conditions tested, as well as effects on bone marrow.

Strengths:

The authors used two mouse models of TB that are representative of different aspects of TB in patients (which they describe well), intending to present a fuller picture of the activity of the tested drug combinations. They conducted a large body of work in these infected mice to evaluate efficacy and also to survey a wide range of parameters that could inform the effect of the treatments on bone marrow and on the immune system. The inclusion of BPa controls (in most studies) and also untreated groups led to a large amount of useful data that has been collected for the mouse models per se (untreated) as well as for BPa - in addition to the BPaS and BPaL combinations which are of particular interest to the authors. Many of these findings related to BPa, BPaL, untreated groups, etc corroborate earlier findings and the authors point this out effectively and clearly in their manuscript. To go further, in general, it is a well-written and cited article with an informative introduction.

Weaknesses:

The authors performed a large amount of work with the drugs given at the doses and dosing intervals started, but at present, there is no exposure data available in the paper. It would be of great value to understand the exposures achieved in plasma at least (and in the lung if more relevant for S) in order to better understand how these relate to clinical exposures that are observed at marketed doses for B, Pa, and L as well as to understand the exposure achieved at the doses being evaluated for S. If available as historical data this could be included/cited. Considering the great attempts made to evaluate parameters that are relevant to clinical adverse events, it would add value to understand what exposures of drug effects such as anemia, weight loss, and bone marrow effects, are being observed. It would also be of value to add an assessment of whether the weight loss, anemia, or bone marrow effects observed for BPaL are considered adverse, and the extent to which we can translate these effects from mouse to patient (i.e. what are the limitations of these assessments made in a mouse study?). For example, is the small weight loss seen as significant, or is it reversible? Is the magnitude of the changes in blood parameters similar to the parameters seen in patients given L? In addition, it is always challenging to interpret findings for combinations of drugs, so the addition of language to explain this would add value: for example, how confident can we be that the weight loss seen for only the BPaL group is due to L as opposed to a PK interaction leading to an elevated exposure and weight loss due to B or Pa?

We totally agree with this critique but the studies suggested by the reviewer are very expensive and

logistically/resource intensive. Data reported in this manuscript was used as preliminary data in a RO1 application to NIH-NIAID that included studies proposed above by this reviewer. The authors are glad to report that the application got a fundable score and is currently under consideration for funding by NIH-NIAID.   The summary of proposed future studies is included in the last paragraph of the discussion in this revised manuscript. 

Turning to the evaluations of activity in mouse TB models, unfortunately, the evaluations of activity in the BALB/c mouse model as well as the spleens of the Kramnik model resulted in CFU below/at the limit of detection and so, to this reviewer's understanding of the data, comparisons between BPaL and BPaS cannot be made and so the conclusion of equivalent efficacy in BALB/c is not supported with the data shown. There is no BPa control in the BALB/c study, therefore it is not possible to discern whether L or S contributed to the activity of BPaL or BPaS; it is possible that BPa would have shown the same efficacy as the 3 drug combinations. It would be valuable to conduct a study including a BPa control and with a shorter treatment time to allow comparison of BPa, BPaS, and BPaL. 

We agree with the reviewer these studies need to be done.  Some of them were recently published by our colleague Dr. Lyons (reference #60 in revised manuscript). The studies proposed by the reviewer will be performed under a new award under consideration for funding by the NIH-NIAID, the summary of future studies is included in the last paragraph of the discussion in this revised manuscript. 

In the Kramnik lungs, as the authors rightly note, the studies do not support any contribution of S or L to BPa - i.e. the activity observed for BPa, BPaL, and BPaS did not significantly differ. Although the conclusions note equivalency of BPaL and BPaS, which is correct, it would be helpful to also include BPa in this statement;

We edited and now included in lines #191 as requested 

It would be useful to conduct a study dosing for a longer period of time or assessing a relapse endpoint, where it is possible that a contribution of L and/or S may be seen - thus making a stronger argument for S contributing an equivalent efficacy to L. The same is true for the assessment of lesions - unfortunately, there was no BPa control meaning that even where equivalency is seen for BPaL and BPaS, the reader is unable to deduce whether L or S made a contribution to this activity.

Added in the future plans in the last paragraph of discussion

“Future studies are already under consideration for funding by NIH-NIAID to understand the pharmacokinetics of mono, binary and ternary combinations of BPaS. These studies also aim to identify the optimal dose level and dosing frequency of each regimen along with their efficacy and relapse free-sterilization potential. Studies are also planned using a model-based pharmacokinetic-pharmacodynamic (PKPD) framework, guided by an existing human BPa PKPD model (reference #61 in revised manuscript), to find allometric human dose levels, dosing frequencies and treatment durations that will inform the experimental design of future clinical studies. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Although this is not a weakness of this paper, a sentence describing how the spectinamide would be administered by aerosolization in humans would be welcomed.

Last paragraph of discussion was added “It is proposed that human use of spectinamides 1599 will be administered using a dry powder formulation delivered by the RS01 Plastiape dry powder inhaler". We already reported on the aerodynamic properties of dry powder spectinamide 1599 within #3 HPMC capsules and delivered from a RS01 Plastiape inhaler device (reference #59 in revised manuscript)

Reviewer #2 (Recommendations For The Authors):

Major comments

The Abstract lacks focus and could more clearly convey the key messages.

Edited as requested 

The two mouse models and why they were chosen need to be described earlier. Currently, it's covered in the first section of the Discussion, but the reader needs to understand the utility of each model in answering the questions at hand before the first results are described, either in the introduction or in the opening section of the results.

Thank you for suggestion, we agree.  We moved the first paragraph in discussion to last paragraph in Introduction. 

Line 130: Please justify the doses and dosing frequency for S. A reference to a published manuscript could suffice if compelling.

The dosing and regimens were previously reported by our groups in ref 21 and 22 in revised manuscript.- 

(21) Robertson GT, Scherman MS, Bruhn DF, Liu J, Hastings C, McNeil MR, et al. Spectinamides are effective partner agents for the treatment of tuberculosis in multiple mouse infection models. J Antimicrob Chemother.

2017;72(3):770–7. 

(22) Gonzalez-Juarrero M, Lukka PB, Wagh S, Walz A, Arab J, Pearce C, et al. Preclinical Evaluation of Inhalational Spectinamide-1599 Therapy against Tuberculosis. ACS Infect Dis. 2021;7(10):2850–63. 

Figures 1 E to H: several "ns" are missing, please add them.

Edited as requested 

Line 184 to 190: suggest moving the body weight plots to a Supplemental Figure, and at least double the size of the histology images to convey the message of lines 192-203.

Please include higher magnification insets to illustrate the histopathological findings. In that same section, please add a sentence or two describing the lesion scoring concept/method. It is a nice added feature, not widespread in the field, and deserves a brief description.

Edited as requested.  We added detailed description for scoring method in M&M under histopathology and lesion scoring

Line 206: please add an introductory sentence explaining why one would expect S to cause (or not) hematological disruption, and why MCHC and RDW were chosen initially (they are markers of xyz). The first part of Figure 3 legend belongs to the Methods.

To address this critique we added in #225-226 “The effect of L in the blood profile of humans and mouse has been reported (references #38-42 in revised manuscript) but the same has not been reported for S” . In line #229-230 we added “Of 20-blood parameters evaluated, two blood parameters were affected during treatment”. 

The first part of Figure 3 legend belongs to the Methods.

We edited Figure 3 to “During therapy of mice in Figure 1, the blood was collected at 1, 2- and 4-weeks posttreatment. The complete blood count was collected in VETSCAN® HM5 hematology analyzer (Zoetis)”.

Line 218: please explain why the 4 blood parameters that are shown were selected, out of the 20 parameters surveyed.

We added an explanation in line 239-240 “out 20-blood parameters evaluated, a total of four blood parameters were affected at 2 and 4-weeks-of treatment”.

Line 243 and again Line 262 (similar to comment Line 206): please add an introductory paragraph explaining the motivation to conduct this analysis and the objective. Can the authors put the experiment in the context of their hypothesis?

To address this critique, we added in line #235-237 “The Nix-TB trial associated the long-term administration of L within the BPaL regimen as the causative agent resulting in anemia in patients treated with the BPaL regimen (5).”

Figure 4C (and the plasma and lung equivalent in the SI). This figure needs adequate labeling of axes: X axis = LOG CFU? Please add tick marks for all plots since log CFU is only shown for the bottom line. Y axes have no units: pg/mL as in B?

Figure legend were edited to add (Y axis:pg/ml) and (X axis; log10CFU).  

Line 255-256: please remove "pronounced" and "profound". There is a range of CFU reduction and cytokine reduction, from minor to major. The correlation trend is clear and those words are not needed.

Edited as requested 

Line 277-289, Figure 6: given the heterogeneity of a C3HeB/FeJ mouse lung (TB infected), and the very heterogeneous cell population distribution in these lungs (Fig. 6A), the validity of whole lung analysis on 2 or 3 mice (the legend should state what 1, 2 and 3 means, individual mice?) is put into question. "F4/80+ cells were observed significantly higher in BPaS compared to UnRx control": Figure S14 suggests a statistically significant difference, but nothing is said about the other cell type, which appears just as much reduced in BPaS compared to UnRx as F4/80+. Overall, sampling the whole lung for these analyses should be mentioned as a limitation in the Discussion.

We agree with the reviewer that "visually" it appears as other populations in addition to F4/80 have statistical significance.  We run again the two way Anova with Tukey test and only the BPaS and UnRx for F4/80 is significant. 

We edited figure S16 (previously S14) to add ns for every comparation.  

In Figure 6A was edited ;  N=2 are 2 mice for Unrx and n=3 mice for BPaL/BPaS each.

Line 355-360: "The BPa and BPaL regimens altered M:E in the C3HeB/FeJ TB model by suppressing myeloid and inducing erythroid lineages" This suggests that altered M:E is not associated with L, putting into question the comparison between BPaS, BPaL, and UnRx. Can the authors comment on how M:E is altered in BPa and not in BPaS?

Our interpretation to this result was that addition of S in our regimen BPsS was capable of restoring the M:E ratio altered by the BPa and BPaL. This interpretation was included in main text in line #263-264 and is also now added to abstract

Line 379: discuss the limitations of working with whole lungs.

Sorry we cannot understand this request. In our studies we always work with whole lungs if the expected course of histopathology/infection among lung lobes is very variable (as is the case of C3HeB/Fej TB model)

Concluding paragraph: "Here we present initial results that are in line with these goals." If such a bold claim is made, there needs to be a discussion on the translatability of the route of administration and the dose of S. Otherwise, please rephrase.

We added the following last paragraph to discussion:

To conclude, the TB drug development field is working towards developing shorter and safer therapies with a common goal of developing new multidrug regimens of low pill burden that are accessible to patients, of short duration (ideally 2-3 months) and consist of 3-4 drugs of novel mode-of-action with proven efficacy, safety, and limited toxicity. Here we present initial results for new multidrug regimens containing inhaled spectinamide 1599 that are in line with these goals. It is proposed that human use of spectinamides 1599 will be administered using a dry powder formulation delivered by the RS01 Plastiape dry powder inhaler.  We already reported on the aerodynamic properties of dry powder spectinamide 1599 within #3 HPMC capsules and delivered from a RS01 Plastiape inhaler device (reference #59 in revised manuscript). Future studies are already under consideration for funding by NIHNIAID to understand the pharmacokinetics of mono, binary and ternary combinations of BPaS. These studies also aim to identify the optimal dose level and dosing frequency of each regimen along with their efficacy and relapse free-sterilization potential. Studies are also planned using a model-based pharmacokinetic-pharmacodynamic (PKPD) framework, guided by an existing human BPa PKPD model (references #60 and 61 in revised manuscript) , to find allometric human dose levels, dosing frequencies and treatment durations that will inform the experimental design of future clinical studies.

Minor edits

Adverse events, not adverse effects (side effects)

Edited as requested

BALB/c (not Balb/c, please change throughout).

Edited as requested

Line 92: replace 'efficacy' with potency or activity.

Edited as requested

"Live" body weight: how is that different from "body weight"? Suggest deleting "live" throughout, or replace with "longitudinally recorded" if that's what is meant, although this is generally implied.

Edited as requested

The last line of Figure 2 legend is disconnected. 

Line 331: delete "human".

Edited as requested

Reviewer #3 (Recommendations For The Authors):

We thank the reviewer for these suggestions.  The data presented in this manuscript with 4 weeks of treatment along with monitoring of effects of therapy in blood, bone marrow and immunity have been submitted for a RO1 application to NIH-NIAID, which have received a fundable score and is under funding consideration. All the points suggested by the reviewer(s) here are included in the research proposed in the RO1 application including manufacturing and physico-chemically characterize larger scale of dry powders of spectinmides and evaluation of their aerodynamic performance for human or animal use; Pharmacokinetics and efficacy studies to determine the optimal dose level and dosing frequency for new multidrug regimens containing spectinamides. These studies include mono, binary and ternary combinations of each multidrug regimen along with their efficacy and relapse free- sterilization potential. These studies will also develop PK/PD simulation-based allometric scaling to aid in human dose projections inhalation. We hope the reviewer will understand all together these studies will last 4-5 years.  

Although I truly appreciate the great efforts of the authors, I suggest that in order to better evaluate the contribution of S versus L to BPa in these models, repeat studies be run that:

(a) include BPa groups to allow the contribution of S and L to be assessed. Included in research proposed RO1 application mentioned above

(b) use shorter treatment times in BALB/c to allow comparisons at end of Tx CFU above the LOD. We have added new data for 2 weeks treatment with BPaL and BPaS in Balb/c mice infected with MTb that was removed from previous submission of this manuscript

(c) use longer treatment times and ideally a relapse endpoint in Kramnik to allow

assessment of L and S as contributors to BPa (i.e. give a chance to see better efficacy of BPaL or BPaS versus BPa) and also measure plasma exposures of all drugs (or lung levels if this is the translatable parameter for S) to allow detection of any large DDI and also understand the translation to the clinic. Related to the safety parameters, it would be really great to understand whether or not the observations for BPaL would be labeled adverse in a toxicology study/in a clinical study, and it would be useful to include information on the magnitude of observations seen here versus in the clinic (eg for the hematological parameters).

The research proposed in the RO1 application mentioned above included extensive PK, extended periods of treatment beyond 1 month of treatment (2-5 months as needed to reach negative culturable bacterial from organs) and of course relapse studies. 

Minor point: I suggest rewording "high safety profile" when describing spectinomides in the intro - or perhaps qualify the length of dosing where the drug is well tolerated

"high safety profile" was replaced by “an acceptable safety profile”

eLife assessment

In this useful study, the authors report the efficacy, hematological effects, and inflammatory response of the BPaL regimen (containing bedaquiline, pretomanid, and linezolid) compared to a variation in which Linezolid is replaced with the preclinical development candidate spectinamide 1599, administered by inhalation in tuberculosis-infected mice. The authors provide convincing evidence that supports the replacement of Linezolid in the current standard of care for drug-resistant tuberculosis. The work will be of interest to those studying tuberculosis treatment regimens.

Reviewer #1 (Public Review):

Summary:<br /> The manuscript entitled A Modified BPaL Regimen for Tuberculosis Treatment<br /> replaces Linezolid with Inhaled Spectinamides by Malik Zohaib Ali et al. is an extension of previous studies by this group looking at the new drug spectinamide 1599. The authors directly compare therapy with BPaL (bedaquiline, pretomanid, linezolid) to a therapy that substitutes spectinamide for linezolid (BPaS). The Spectinamide is given by aerosol exposure and the BPaS therapy is shown to be as effective as BPaL without adverse effects. The work is rigorously performed and analyses of the immune responses are consistent with curative therapy.

Strengths:<br /> 1) This group uses 2 different mouse models to show the effectiveness of the BPaS treatment.<br /> 2)Impressively the group demonstrates immunological correlates associated with Mtb cure with the BPaS therapy.<br /> 3)Linezolid is known to inhibit ribsomes and mitochondria whereas spectinaminde does not. The authors clearly demonstrate the lack of adverse effects of BPaS compared to BPaL.

Weaknesses:<br /> 1) Although this is not a weakness of this paper, a sentence describing how the spectinamide would be administered by aerosolization in humans would be welcomed.

Reviewer #2 (Public Review):

Summary:<br /> Replacing linezolid (L) with the preclinical development candidate spectinamide 1599, administered by inhalation, in the BPaL standard of care regimen achieves similar efficacy, reduces hematological changes and por-inflammatory responses.

Strengths:<br /> The authors not only measure efficacy but also quantify histological changes, hematological responses and immune responses, to provide a comprehensive picture of treatment response and the benefits of the L to S substitution.

The authors generate all data in two mouse models of TB infection, each reproducing different aspects of human histopathology.

Extensive supplementary figures ensure transparency.

Weaknesses:<br /> Articulation of objectives and hypotheses can be improved, as suggested below.

Reviewer #3 (Public Review):

Summary:<br /> In this paper, the authors sought to evaluate whether the novel TB drug candidate, spectinamide 1599 (S), given via inhalation to mouse TB models, and combined with the drugs B (bedaquiline) and Pa (pretomanid), would demonstrate similar efficacy to that of BPaL regimen (where L is linezolid). Because L is associated with adverse events when given to patients longterm, and one of those is associated with myelosuppression (bone marrow toxicity) the authors also sought to assess blood parameters, effects on bone marrow, immune parameters/cell effects following treatment of mice with BPaS and BPaL. They conclude that BPaL and BPaS have equivalent efficacy in both TB models used and that BPaL resulted in weight loss and anemia (whereas BPaS did not) under the conditions tested, as well as effects on bone marrow.

Strengths:<br /> The authors used two mouse models of TB that are representative of different aspects of TB in patients (which they describe well), intending to present a fuller picture of the activity of the tested drug combinations. They conducted a large body of work in these infected mice to evaluate efficacy and also to survey a wide range of parameters that could inform the effect of the treatments on bone marrow and on the immune system. The inclusion of BPa controls (in most studies) and also untreated groups led to a large amount of useful data that has been collected for the mouse models per se (untreated) as well as for BPa - in addition to the BPaS and BPaL combinations which are of particular interest to the authors. Many of these findings related to BPa, BPaL, untreated groups etc corroborate earlier findings and the authors point this out effectively and clearly in their manuscript. To go further, in general, it is a well written and cited article with an informative introduction.

Weaknesses:<br /> The authors performed a large amount of work with the drugs given at the doses and dosing intervals stated, but there is no exposure data available at this time. The authors intend to evaluate exposure-effect relationships in future work. An understanding of the exposures at which the efficacy and adverse effects are seen will assist in the translation of these findings to the clinic.<br /> In addition, it is always challenging to interpret findings for combinations of drugs and for now, the data available cannot attribute confidence to the weight loss seen for only the BPaL group to L specifically, as opposed to a PK interaction leading to an elevated exposure and weight loss due to B or Pa. It is not yet possible, then to state that what is seen are "L-associated AEs" - this is assumed only.<br /> The evaluations of activity in the BALB/c mouse model as well as the spleens of the Kramnik model resulted in CFU below/at the limit of detection so comparisons between BPaL and BPaS cannot be made and so the conclusion of equivalent efficacy in BALB/c is not supported with the data shown. There is no BPa control in the BALB/c study, therefore it is not possible to discern whether L or S contributed to the activity of BPaL or BPaS. The same is true for the assessment of lesions - unfortunately, there was no BPa control meaning that even where equivalency is seen for BPaL and BPaS, the reader is unable to deduce whether L or S made a contribution to this activity.<br /> Although these weaknesses limit what we can learn from the current body of data, the authors note that further studies will be done to increase understanding of the points above.

eLife assessment

ImmCellTyper presents a useful toolkit for CyTOF data analysis, integrating BinaryClust for semi-supervised clustering and cell type annotation. The evidence supporting the findings is convincing, with appropriate and validated methodology. This tool will be helpful to researchers in immunology and cytometry, offering a robust solution for cell type identification and differential analysis.

Reviewer #3 (Public Review):

Summary:

ImmCellTyper is a new toolkit for Cytometry by time-of-flight data analysis. It includes BinaryClust, a semi-supervised clustering tool (which takes into account the prior biological knowledge), designed for automated classification and annotation of specific cell types and subpopulations. ImmCellTyper also integrates a variety of tools to perform data quality analysis, batch effect correction, dimension reduction, unsupervised clustering, and differential analysis.

Strengths:

The proposed algorithm takes into account the prior knowledge.<br /> The results on different benchmark indicates competitive or better performance (in terms of accuracy and speed) depending on the method.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

This manuscript presented a useful toolkit designed for CyTOF data analysis, which integrates 5 key steps as an analytical framework. A semi-supervised clustering tool was developed, and its performance was tested in multiple independent datasets. The tool was compared to human experts as well as supervised and unsupervised methods. 

Strengths: 

The study employed multiple independent datasets to test the pipeline. A new semi-supervised clustering method was developed. 

Weaknesses: 

The examination of the whole pipeline is incomplete. Lack of descriptions or justifications for some analyses. 

We thank the reviewer’s overall summary and comments of this manuscript. In the last part of the results, we showcased the functionalities of ImmCellTyper in covid dataset, including quality check, BinaryClust clustering, cell abundance quantification, state marker expression comparison within each identified cell types, cell population extraction, subpopulation discovery using unsupervised methods, and data visualization etc. We added more descriptions in the text based on the reviewer’s suggestions. 

Reviewer #2 (Public Review): 

Summary: 

The authors have developed marker selection and k-means (k=2) based binary clustering algorithm for the first-level supervised clustering of the CyTOF dataset. They built a seamless pipeline that offers the multiple functionalities required for CyTOF data analysis. 

Strengths: 

The strength of the study is the potential use of the pipeline for the CyTOF community as a wrapper for multiple functions required for the analysis. The concept of the first line of binary clustering with known markers can be practically powerful. 

Weaknesses: 

The weakness of the study is that there's little conceptual novelty in the algorithms suggested from the study and the benchmarking is done in limited conditions. 

We thank the reviewer’s overall summary and comments of this manuscript. While the concept of binary clustering by k-means is not novel, BinaryClust only uses it for individual markers to identify positive and negative cells, then combine it with the pre-defined matrix for cell type identification. This has not been introduced elsewhere. Furthermore, ImmCellTyper streamlines the entire analysis process and enhances data exploration on multiple levels. For instance, users can evaluate functional marker expression level/cellular abundance across both main cell types and subpopulations; Also, this computational framework leverages the advantages of both semi-supervised and unsupervised clustering methods to facilitate subpopulation discovery. We believe these contributions warrant consideration as advancements in the field.  

As for the benchmarking, we limited the depth only to main cell types rather than subpopulations. The reason is because we only apply BinaryClust to identify main cell types; For the cell subsets discovery, unsupervised methods integrated in this pipeline has already been published and widely used by the research community. Therefore, it does not seem to be necessary for additional benchmarking.

Reviewer #3 (Public Review): 

Summary: 

ImmCellTyper is a new toolkit for Cytometry by time-of-flight data analysis. It includes BinaryClust, a semi-supervised clustering tool (which takes into account prior biological knowledge), designed for automated classification and annotation of specific cell types and subpopulations. ImmCellTyper also integrates a variety of tools to perform data quality analysis, batch effect correction, dimension reduction, unsupervised clustering, and differential analysis. 

Strengths: 

The proposed algorithm takes into account the prior knowledge. 

The results on different benchmarks indicate competitive or better performance (in terms of accuracy and speed) depending on the method. 

Weaknesses: 

The proposed algorithm considers only CyTOF markers with binary distribution. 

We thank the reviewer’s overall summary and comments of this manuscript. Binary classification can be considered as an imitation of human gating strategy, as it is applied to each marker. For example, when characterizing the CD8 T cells, we aim for CD19-CD14-CD3+CD4- population, which is binary in nature (either positive and negative) and follows the same logic as the method (BinaryClust) we developed. Results indicated that it works very well for well-defined main cell lineages, particularly when the expression of the defining marker is not continuous. However, the limitation is for subpopulation identification, because a handful makers behave in a continuum manner, so we suggest unsupervised method after BinaryClust, which also brings another advantage of identifying unknown subsets beyond our current knowledge, and none of the semi-supervised tools can achieve that. To address the reviewer’s concern, we considered the limitation of binary distribution, but it does not profoundly affect the application of the pipeline.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Many thanks for the reviewers’ comments and suggestions, please see below the point-to-point response:

(1) The style of in-text reference citation is not consistent. Many do not have published years.

The style of the reference citation has been revised and improved.  

(2) The font size in the table of Figure 1 is too small, so is Figure 2. 

The font size has been increased.

(3) Is flowSOM used as part of BinaryClust? How should the variable running speed of BinaryClust be interpreted, given that it is occasionally slower and sometimes faster than flowSOM in the datasets?

To answer reviewer’s question, flowSOM is not a part of BinaryClust. They are separate clustering methods that have been incorporated into the ImmCellTyper pipeline. As described in Figure 1, BinaryClust, a semi-supervised method, is used to classify the main cell lineages; while flowSOM, an unsupervised method, is recommended here for further subpopulation discovery. So, they operate independently of each other. To avoid confusions, we slightly modified Figure 1 for clarification.

Regarding the variability in running speed in Figure 4. The performance of algorithms can indeed be influenced by the characteristics of the datasets, such as size and complexity. The differences observed between the covid dataset and the MPN dataset, such as marker panel, experimental protocol, and data acquisition process etc., could account for this variation. Our explanation is that flowSOM suits better the data structure of covid dataset, which might be the reason why it is slightly faster to analyse compared to the MPN dataset. Moreover, for the covid dataset, the runtime for both BinaryClust and flowSOM is less than 100s, and the difference is not notable. 

(4) In the Method section ImmCellTyper workflow overview, it is difficult to link the description of the pipeline to Figure 8. There are two sub-pipelines in the text and seven steps in the figure. What are their relations? Some steps are not introduced in the text, such as Data transformation and SCE object construction. What is co-factor 5?

Figure 8 provides an overview of the entire workflow for CyTOF data analysis, starting from the raw fcs file data and proceeding until downstream analysis (seven steps). But the actual implementation of the pipeline was divided into two separate sections, as outlined in the vignettes of the ImmCellTyper GitHub page (https://github.com/JingAnyaSun/ImmCellTyper/tree/main/vignettes).

Users will initially run ‘Intro_to_batch_exam_correct’ to perform data quality check and identify potential batch effects, followed by ‘Intro_to_data_analysis’ for data exploration. We agree with the reviewer that the method for this section is a bit confusing, so we’ve added more description for clarification.

In processing mass cytometry data, arcsine transformation is commonly applied to handle zero values, skewed distributions, and to improve visualization as well as clustering performance. The co-factor here is used as a parameter to scale down the data to control the width of the linear region before arcsine transformation. We usually get the best results by using co-factor 5 for CyTOF data.   

(5) For differential analysis, could the pipeline analyze paired/repeated samples?

For the statistical step, ImmCellTyper supports both two-study group comparison using Mann-Whitney Wilcoxon test, and multiple study group comparison (n>2) using Kruskal Wallis test followed by post hoc analysis (pairwise Wilcoxon test or Dunn’s test) with multiple testing correction using Benjamini-Hochberg Procedure.

Certainly, this pipeline allows flexibilities, users can also extract the raw data of cell frequencies and apply suitable statistical methods for testing.

(6) In Figure 2A, the range of the two axes is different for Dendritic cells, which could be misleading. Why the agreement is bad for dendritic cells?

The range for the axes is automatically adapted to the data structure, which explains why they may not necessarily be equal. The co-efficient factor for the correlation of DCs is 0.958, compared to other cell types (> 0.99), it is relatively worse but does not indicate poor agreement.

Moreover, the abundance of DCs is much less than other cell types, comprising approximately 2-5% of whole cells. As a result, even small differences in abundance may appear to as significant variations. For example, a difference of 1% in DC abundance represents a 2-fold change, which can be perceived as substantial.

Overall, while the agreement for DCs may appear comparatively lower, it is not necessarily indicative of poor performance, considering both the coefficient factor and the relative abundance of DCs compared to other cell types.

(7) In the Results section BinaryClust achieves high accuracy, what method was used to get the p-value, such as lines 212, 213, etc.?

The accuracy of BinaryClust was tested using F-measure and ARI against ground truth (manual gating), the detailed description/calculation can be found in methods. For line 212 and 213, the p-value was calculated using ANOVA for the interaction plot shown in Figure 3. We’ve now added the statistical information into the figure legend.   

(8) The performance comparison between BinaryClust and LDA is close. The current comparison design looks unfair. Given LDA only trained using half data, LDA may outperform BinaryClust.

It is true that LDA was trained using half data, which is because this method requires manual gating results as training dataset to build a model, then apply the model to the rest of the files to label cell types. Here we used 50% of the whole dataset as training set. We are of course very happy to implement any additional suggestions for a better partition ratio.

(9) There are 5 key steps in the proposed workflow. However, not every step was presented in the Results.

Thanks for the comments. The results primarily focused on demonstrating the precision and performance of BinaryClust in comparison with ground truth and existing tools. Additionally, a case study showcasing the application/functions of the entire pipeline in a dataset was also presented. Due to limitation in space, the implementation details of the pipeline were described in the method section and github documentations, which users/readers can easily access.

Reviewer #2 (Recommendations For The Authors): 

The tools suggested by the authors could be potentially useful to the community. However, it's difficult to understand the conceptual novelty of the algorithms suggested here. The concept of binary clustering has been described before (https://doi.org/10.1186/s12859-022-05085-z, https://doi.org/10.1152/ajplung.00104.2022), and it mainly utilizes k-means clustering set to generate binary clusters based on selected markers. Other algorithms associated with the package are taken from other studies. 

We acknowledge the reviewer’s comment regarding the novelty of our method. While the concept of binary clustering by k-means has been previously described to transcriptome data, our approach applies it to CyTOF data analysis, which has not been introduced elsewhere. Furthermore, ImmCellTyper streamlines the entire analysis process and enhances data exploration on multiple levels. For instance, users can evaluate functional marker expression level/cellular abundance across both main cell types and subpopulations; Also, as stated in the manuscript, this computational framework leverages the advantages of both semi-supervised and unsupervised clustering methods to facilitate subpopulation discovery. We believe these contributions warrant consideration as advancements in the field.  

In addition, the benchmarking of clustering performance, especially to reproduce manual gating and comparison to tools such as flowSOM is not comprehensive enough. The result for the benchmarking test could significantly vary depending on how the authors set the ground truth (resolution of cell type annotations). The authors should compare the tool's performance by changing the depth of cell type annotations. Especially, the low abundance cell types such as gdT cells or DCs were not effectively captured by the suggested methods. 

Thanks for the comment. We appreciate the reviewer’s concern. However, as illustrated in figure 1, our approach uses BinaryClust, a semi-supervised method, to identify main cell types rather than directly targeting subpopulations. The reason is because semi-supervised method relies on users’ prior definition thus is limited to discover novel subsets. In the ImmCellTyper framework, unsupervised method was subsequently applied for subset exploration following the BinaryClust step.

Regarding benchmarking, we focused on testing the precision of BinaryClust for main cell type characterization, because it is what the method is used for in the pipeline, and we believe this is sufficient. As for the cell subsets discovery, the unsupervised methods we integrated has already been published and widely used by the research community. Therefore, it does not seem to be necessary for additional benchmarking.

Moreover, as shown in Figure 3 and Table 1, our results indicated that the F-measure for DCs and gdT cells in BinaryClust is 0.80 and 0.92 respectively, which were very close to ground truth and outperformed flowSOM, demonstrating its effectiveness. 

We hope these clarifications address the reviewer’s concern.

Minor comments: 

(1) In Figure 4, it's perplexing to note that BinaryClust shows the slowest runtime for the COVID dataset, compared to the MPN dataset, which features a similar number of cells. What causes this variation? Is it dependent on the number of markers utilized for the clustering? This should be clarified/tested. 

Thanks for the comment, but we are not sure that we fully understand the question. As shown in figure 4 that BinaryClust has slightly higher runtime in MPN dataset than covid dataset, which is reasonable because and the cell number in MPN dataset is around 1.6 million more than covid dataset.

(2) Some typos are noted: 

- DeepCyTOF and LDA use a maker expression matrix extracted → "marker"?* 

Corrected.

- Datasets(Chevrier et al.)which → spacing* 

Corrected.

- This is due to the method's reliance → spacing*

Corrected.

Reviewer #3 (Recommendations For The Authors): 

Is it possible to accommodate more than two levels within the clustering process, i.e., can the proposed semi-supervised clustering tool be extended to multi-levels instead of binary?

Thanks for the comments. Binary classification can be considered as an imitation of human gating strategy, as it is applied to each marker. For example, when characterizing the CD8 T cells, we aim for CD19-CD14-CD3+CD4- population, which is binary in nature (either positive and negative) and follows the same logic as the method (BinaryClust) we developed. Results indicated that it works very well for well-defined main cell lineages. However, the limitation is for subpopulation identification, because a handful of makers behave in a continuum manner, so we would suggest unsupervised method after BinaryClust, which also brings another advantage of identifying unknown subsets beyond our current knowledge, and none of the semi-supervised tools can achieve that. To answer the reviewer’s question, it is possible to set the number to 3,4,5 rather than just 2, but considering the design and rationale of the entire framework (as describe in the manuscript and above), it doesn’t seem to be necessary.

Could you please comment on why on the COVID dataset, BinaryClust was slower as compared to flowSOM?

Thanks for the question. The performance of algorithms can indeed be affected by the characteristics of the datasets, such as their size and complexity. The covid and MPN datasets differ in various aspects including marker panel, experimental protocol, and data acquisition process, among others, which wound account for the observed variation in speed. So, our explanation is flowSOM suits better for the structure of covid dataset than MPN dataset.  Additionally, for covid dataset, both BinaryClust and flowSOM have runtimes of less than 100s, and the difference between the two isn’t particularly dramatic.

Minor errors: 

Line#215 "(ref) " reference is missing

Added.

Figure 3, increase the font of the text in order to improve readability. 

Increased.

Line#229 didn't --> did not. 

Corrected

Line#293 repetition of the reference. 

The repetition is due to the format of the citation, which has been revised.