Author Response:

Reviewer #1 (Public Review):

This manuscript investigates the gene regulatory mechanisms that are involved in the development and evolution of motor neurons, utilizing cross-species comparison of RNA-sequencing and ATAC-sequencing data from little skate, chick and mouse. The authors suggest that both conserved and divergent mechanisms contribute to motor neuron specification in each species. They also claim that more complex regulatory mechanisms have evolved in tetrapods to accommodate sophisticated motor behaviors. While this is strongly suggested by the authors' ATAC-seq data, some additional validation would be required to thoroughly support this claim.

Strengths of the manuscript:

1) The manuscript provides a valuable resource to the field by generating an assembly of the little skate genome, containing precise gene annotations that can now be utilized to perform gene expression and epigenetic analyses. The authors take advantage of this novel resource to identify novel gene expression programs and regulatory modules in little skate motor neurons.

2) Cross-species RNA-seq and ATAC-seq data comparisons are combined in a powerful approach to identify novel mechanisms that control motor neuron development and evolution.

Weaknesses:

1) It is surprising that the analysis of RNA-seq datasets between mouse, chick, and little skate only identified 5 genes that are common between the 3 species, especially given the authors' previous work identifying highly conserved molecular programs between little skate and mouse motor neurons, including core transcription factors (Isl1, Hb9, Lhx3), Hox genes and cholinergic transmission genes. This raises some questions about the robustness of the sequencing data and whether the genes identified represent the full transcriptome of these motor neurons.

To address reviewer #1’s questions, we have generated RNA sequencing data with mouse forelimb MNs and re-analyzed the RNA-seq data using only the homologous MN populations (Figure 3) among different species. As a result, many genes (1038 genes) are commonly expressed in MNs in different species, including many known MN marker genes. In the result section, we have added the following:

“The evolution of genetic programs in MNs was investigated unbiasedly by comparing highly expressed genes in pec-MNs (percentile expression > 70) of little skate with the ones from MNs of mouse and chick, two well-studied tetrapod species. In order to compare gene expression with homologous cell types from each species, we performed RNA sequencing on forelimb MNs of mouse embryos at embryonic day 13.5 (e13.5) and wing level MNs of chick embryos at Hamburger-Hamilton (HH) stage 26–27…”

We have also compared our re-analysis with previous results in Figure 2–figure supplement 1, shown above. Most of the fin MN genes (21/24) are highly expressed in pecMNs (percentile > 70), consistent with the previous in situ experiments. In the Results we have added the following:

“Although the total number of DEGs are different from the previous data (592 vs. 135 genes in pec-MN DEGs), which might be caused by different statistical analysis with different reference genome, previous RNA-seq data based on de novo assembly and annotation using zebrafish was mostly recapitulated in our DEG analysis based on our new skate genome (21 out of 24 previous fin MN marker genes have the expression level ranked above 70th percentile in Pec-MNs; Figure 2‒figure supplement 1).”

2) The authors suggest based on analysis of binding motifs in their ATAC-seq data that the greater number of putative binding sites in the mouse MNs allows for a higher complexity of regulation and specialization of putative motor pools. This could certainly be true in theory but needs to be further validated. The authors show FoxP1 as an example, which seems to be more heavily regulated in the mouse, but there is no evidence that FoxP1 expression profile is different between mouse and skate. It is suggested in Fig.5 that FoxP1 might be differentially regulated by SnaiI in mouse and skate but the expression of SnaiI in MNs in either species is not shown.

We have added further discussion and data about differential expression of Foxp1 in mouse and little skate in Figure 5–figure supplement 16 and have discussed as follows:

“Foxp1, the major limb/fin MN determinant appears to be differentially regulated in tetrapod and little skate. Although Foxp1 is expressed in and required for the specification of all limb MNs in tetrapods, Foxp1 is downregulated in Pea3 positive MN pools during maturation in mice (Catela et al., 2016; Dasen et al., 2008). In addition, preganglionic motor column neurons (PGC MNs) in the thoracic spinal cord of mouse and chick express half the level of Foxp1 expression than limb MNs. Although PGC neurons have not yet been identified in little skate, we tested the expression level of Foxp1 using a previously characterized tetrapod PGC marker, pSmad. We observed that Foxp1 is not expressed in MNs that express pSmad (Figure 5‒figure supplement 3). Since there is currently no known marker for PGC MNs in little skate, our conclusion should be taken with caution.”

As for Snai1, in the revision we performed a motif enrichment analysis with an unbiased gene list where Snai1 didn’t show up. However, when we performed an RNA in situ hybridization experiment for Snai1 (Figure 5–figure supplement 3), we found that Snai1 is expressed in MNs of both mouse and little skate, but not in chick, which has been shown previously (Cheung et al., 2005). In order to examine the function of Snai1 in the regulation of Foxp1 expression, we ectopically expressed Snai1 in chick spinal cord by performing in ovo electroporation. However, we did not detect any changes in Foxp1. Instead we observed an increase in the number of neurons and abnormal MN exits from the spinal cord, which is the reminiscent of a previous observation (Zander et al., 2014). Although we did not detect any changes in Foxp1 expression, we cannot rule out the possibility that Snai1 regulates Foxp1 in mouse and little skate, which may require a gene knock out experiment. Because binding sites of Snai1 were not enriched in the new gene sets that we analyzed in the revision, we have not further discussed the Snai1 in the text.

3) In their discussion section the authors state that they found both conserved and divergent molecular markers across multiple species but they do not validate the expression of novel markers in either category beyond RNA-seq, for example by in situ or antibody staining.

We have added RNA in situ hybridization results in Figure 3C and Figure 3–figure supplement 1 and 2. Most of the genes were expressed in tissues in accordance with the sequencing results (6 out of 9 common MN genes; 4 out of 6 mouse specific genes; 5 out of 7 skate specific genes). Specifcally, Uchl1, Slc5a7, Alcam, and Serinc1 are expressed in MNs of all three species; Coch, Ppp1rc, Ctxn1, and Clmp are expressed in MNs of mouse but not in MNs of other species; Eya1, Etv5, Dnmbp, and Spint1 are expressed in MNs of skate but not in MNs of other species. In the result section, we have summarized the results as follow:

“These results were validated by performing RNA in situ hybridization in tissue sections on a subset of species-specific genes …”

Author Response

Reviewer #2 (Public Review):

Regulation of NAD and its intermediary metabolites is of critical importance in axon degeneration and neurodegenerative disease. Mounting evidence supports a scenario in which low NAD, and high NMN triggers axon degeneration by competitive allosteric inhibition/activation of SARM1. Strategies to increase NAD levels and/or lower NMN levels provide neuroprotection in a variety of contexts. NAD metabolism is a partially conserved process, however, there are key differences in pathway routes and dynamics between model organisms used for NAD research (yeast, worm, fly, zebrafish, mouse/mammalian systems). Drosophila is a key model organism for axon degenerative research based on its ease of use and range of available genetic tools, in addition, the effector of axon degeneration - SARM1 - was first identified in the fly. As Drosophila has some key differences in the NAD synthesis pathways to mammalian systems it is important to test and develop tools to enable exploration of these pathways on the fly. Llobet Rosell and colleagues have developed clear and demonstrable tools in Drosophila for exploring NAD-related axon degenerative pathways by modulating the use of NMN via the addition of NMN consuming and NMN generating enzymes. They utilize Drosophila genetics to adequately support the claims made in the manuscript. Importantly, the authors well-demonstrate that consuming NMN through an alternate route to NaMN provides neuroprotection and that the neuroprotective components of low NMN are upstream of SARM1. These should be useful tools for neuroscientists in the future to use Drosophila for neurodegenerative research.

Strengths:

• Clear demonstration that low NMN provides neuroprotection using novel, stable, enzymatic depletion of NMN (to NaMN).

• Development of a novel Drosophila tool (NMN-D transgenics) to explore NMN metabolism in vivo, including a stabilized version to permit chronic NMN depletion.

• Metabolomic profiles across the pathway to show all pathway changes (not just isolated NMN or NAD assays). • Neurodegenerative assays that include both histological outcomes (axon degeneration) but also circuitry/functional outcomes. Data from both series of experiments all support each other.

• Assessment of other known potent axon degenerative genes via genetics in combination with the tools developed. • Staging of the molecular processes by strategic ablation of the inhibitory ARM domain on SARM1 (dSarm deltaARM). These experiments suggest that low NAD AND high NMN (i.e. ratio between the two) is the critical factor that drives axon degeneration. Once NAD is low, axon degeneration cannot be recovered by further lowering of NMN. The dSarm delta-ARM and dnmnat sgRNAs experiments support a hypothesis in that (high) NMN triggers, but doesn't, execute axon degeneration.

We appreciate his recognition of the quality of our research.

Weaknesses:

• The authors use murine NAMPT (mNAMPT) to increase NMN. The degeneration assays support the hypotheses made, yet mNAMPT doesn't actually increase NMN. Thus it is unclear in this setting whether mNAMPT promotes axon degeneration by an NMN-related mechanism or through another route. It is also unclear as to why the murine form was chosen versus a human or other orthologues, or changing the metabolism of the intrinsic pathway (NR and NRK).

Why mNAMPT:

We decided to use mouse NAMPT (mNAMPT) because it was readily available by Giuseppe Orsomando (Amici et al., 2017), and because we did not have access to human NAMPT (hNAMPT).<br /> We agree with the observation that under physiological conditions, the expression of mNAMPT does not change NMN. However, we argue that after injury, once dNmnat is degraded, the additional NMN synthesis provided by mNAMPT expression (in addition to dNrk), leads to a faster NMN accumulation. It is supported by the observation that NMNAT2 is more labile than NAMPT in mammals (Gilley and Coleman, 2010; Stefano et al., 2015).

• The authors use metabolic profiling to look at the individual metabolites during axon degenerative evens and treatments however it is unclear if any of these proteins or genes change as a consequence. This is likely not important for understanding the findings however, might be helpful in explaining the mNAMPT data.

We agree with the idea to test whether there is a change induced at the mRNA or protein level when the metabolic flux is altered. To do this, first, we measured the relative expression levels of axon death and NAD+ synthesis genes (Figure 2 – figure supplement 1B). Then, we measured potential changes upon mNAMPT expression (Figure 4 – figure supplement 1). Importantly, while the Gal4-driven expression resulted in an increase of relative mNAMPT transcript abundance from 30 to 12’000, the change observed in the other genes was not notable. Importantly, compared to Actin–Gal4, dnrk is 2-fold lower in UAS-mNAMPT and Actin > mNAMPT backgrounds (control vs. experiment, respectively). Thus, overall, there appears to be no change in mRNAs of either axon death or NAD+ synthesis genes.

In the results, we changed the text accordingly:

"We then tested the effect of mNAMPT on the NAD+ metabolic flux in vivo. Surprisingly, NAM, NMN, and NAD+ levels remained unchanged under physiological conditions (Figure 4C). However, we noticed 3-fold higher NR and a moderate but significant elevation of ADPR and cADPR levels upon mNAMPT overexpression (Figure 4C). We also asked whether mNAMPT impacts on NAD+ homeostasis thereby altering the expression of axon death or NAD+ synthesis genes. Besides the expected significant increase in the Gal4-mediated expression of mNAMPT, we did not observe any notable changes at the mRNA level (Figure 4 – figure supplement 1)."

• The authors repeatedly introduce a novel PncC antibody. However, no details on this, its generation, or its testing are found within the manuscript as presented. The antibody detects with several bands. The authors speculate that this could be a degradation product but nothing substantial is shown.

In Materials and methods, we added a new section:

"PncC antibody generation Rabbit anti-PncC antibodies were generated by Lubioscience under a proprietary protocol. The immunogen used was purified from Escherichia coli, strain K12, corresponding to the full protein sequence of NMN-D. The amino acid sequence is the following: MTDSELMQLSEQVGQALKARGATVTTAESCTGGWVAKVITDIAGSSAWFERGFVTYSNEAKAQMIGVREETLAQHGAVSEPVVVEMAIGALKAARADYAVSISGIAGPDGGSEEKPVGVWFAFATARGEGITRRECFSGDRDAVRRQAT AYALQTLWQQFLQNT"

We also updated the results referencing it.

"We found that both wild-type and enzymatically dead NMN-D enzymes are equally expressed in S2 cells, as detected by newly generated PncC antibodies (Materials & Methods, Figure 1–figure supplement 2). Notably, we observed two immunoreactivities per lane, with the lower band being a potential degradation product."

In addition, we now provide evidence why we believe that the upper band is NMN-D, while the lower one is a degradation product. In the figure attached below, the samples of the first five lanes were denatured at 70 °C, while the samples of the last two lanes were denatured at 95 °C (each for 10 min, respectively). The resulting Western blot shows that at 70 °C, there is more unspecific background, but no lower degradation product, while at 95 °C, the background is drastically reduced; however, there is a lower degradation product appearing. NMN-D is indicated by an asterisk. We feel that it is important to show this data here in the rebuttal. But we feel that it would add confusion to the readers in the manuscript.

• Olfactory receptor neuron degeneration assays are shown in Fig1 but no data is presented with it to support the images.

We agree that a quantification would support our observation. However, it is difficult to precisely quantify individual axons in the ORN injury assay, for two main reasons:

1. Severed axons are often bundled, thus the exact number cannot be scored.

2. Due to the removal of the cell body, the axonal GFP intensity decreases over time, due to the absence of mCD8::GFP synthesis. It adds another level of difficulty. Nevertheless, we added numbers to each example in Figure 1E and D, where we quantified the % of brains where severed preserved axons were observed, similar to Figure 2 in (MacDonald et al., 2006).

In the results section, we changed the text as indicated below:

"We extended the ORN injury assay and found preservation at 10, 30, and 50 dpa (Figure 1E). While quantifying the precise number of axons is technically not feasible, severed preserved axons were observed in all 10, 30, and 50 dpa brains, albeit fewer at later time points (MacDonald et al., 2006). Thus, high levels of NMN-D confer robust protection of severed axons for multiple neuron types for the entire lifespan of Drosophila."

In the Figure 1 legend, we changed the text accordingly:

"D Low NMN results in severed axons of olfactory receptor neurons that remain morphologically preserved at 7 dpa. Examples of control and 7 dpa (arrows, site of unilateral ablation). Lower right, % of brains with severed preserved axon fibers. E Low NMN results in severed axons that remain morphologically preserved for 50 days. Representative pictures of 10, 30, and 50 dpa, from a total of 10 brains imaged for each condition (arrows, site of unilateral ablation). Lower right, % of brains with severed preserved axon fibers."

Author Response

eLife assesssment:

This paper conducts human and rodent experiments of non-invasive diffusion MRI estimates of axon diameter with the aim to establish whether these estimates provide biologically specific markers of axonal degeneration in MS. It will be of interest to researchers developing quantitative MRI methods and scientists studying neurodegeneration. The experiments provide evidence for the sensitivity of these markers, but do not directly validate axon diameter and do not reflect common pathological mechanisms across rodents and humans.

We thank the Editor for the appreciation of our work. Thanks to the addition of an extensive electron microscopy paradigm, we now include a direct validation of axonal damage and expand on the common pathological mechanisms across the two species. The new results are detailed in the manuscript and summarized in Fig. 3 in the manuscript

Reviewer #1 (Public Review):

1.1 My primary concern relates to how meaningful the human-rodent comparisons are, and whether these comparisons really advance our understanding of AxCaliber estimates in MS. I applaud the aim to conduct "matched" experiments in both rodent models and human disease. It is a strength that the experiments are aligned with respect to the MRI measurements (although there are some caveats to this mentioned below). But beyond that, the overlap is not what one might hope for: the pathology would seem to be very distinct in humans and rodents, and the histological validation is not specific to what the MRI measurements claim to estimate. To summarize the main findings: (i) in a rat model of general axonal degeneration, axon calibre estimates correlate with neurofilaments; (ii) in MS in humans, axon calibre estimates correlate with demyelinating lesions. This gives a picture of AxCalibre estimates correlating with neuropathology, but is this something that has not already been established in the literature? If the aim is to validate AxCaliber, then there is a logic in using a rodent model that isolates alterations to axonal radius, but what then does this add to the existing literature in that space? If the aim is to study MS (for which AxCaliber results have been previously reported in Huang et al), then why not use a rodent model of MS?

We thank the reviewer for their very insightful comments. Indeed, multiple sclerosis (MS) is a chronic neuroinflammatory and neurodegenerative disease of unknown etiology. An enormous effort has been made to obtain animal models that simulate the pathogenesis of this disease. However, while several models exist recapitulating distinct aspects of the disease (mostly related to demyelination), MS fundamentally remains a disease that only affects humans. This does not mean that EAE or lysolecithin models do not provide information on specific aspects and are therefore valuable. In fact, we believe that trying to replicate the pathological mechanisms of this disease in an animal model goes beyond the scope of the present work. In this work, our intention is to validate a biomarker of axonal damage preclinically, and for this, we use a model of axonal degeneration. We do not claim that this model should be valid to capture the complex clinical and pathological manifestation of MS, but we do think that it is a necessary step to ensure MRI sensitivity to axonal pathology. Why necessary? Because all the available (very limited) MRI literature which provides some form of validation: i) only focuses on healthy tissue, and ii) has an n of 1. Our preclinical paradigm gives conclusive evidence that the MRI axonal diameter proxy detects axonal damage as an increase in the mean diameter. This is now detailed in the discussion.

After this necessary preclinical validation, we then apply the same framework to a human disease like MS that, among other manifestations, is believed to also cause axonal pathology. The improvements with respect to the one published work about axonal diameter in MS are: i) the whole brain analysis, which allowed us to characterize the extent of these early alterations outside the demyelinated lesions; and ii) the larger sample size, which allowed us to uncover an association with disease duration, strengthening our hypothesis about increased axonal diameter being a marker of early disease (new Fig. 5).

Regarding the nonspecificity of histological validation, we thank the reviewer for this insightful comment, which triggered an additional analysis that we believe has added further value to the paper. Using electron microscopy, we found that in our model of neurodegeneration, axonal damage is indeed reflected as an increase in axon diameter (new Fig. 3). These recent findings strongly support the validation of our noninvasive diffusion MRI estimates of axon diameter alterations as an early-stage hallmark of normal-appearing tissue in MS.

Coming back to the comparison between pathology in humans and in rodents, the EM data also support our choice of preclinical model, showing axonal swelling, the same phenomenon reported and characterized in recent postmortem histological data in the normal-appearing white matter of MS patients (Luchicchi et al., Ann Neurol 2021) and in lesions (Fisher et al. Ann Neurol 2007).

All in all, we are confident that the new data supports the validity of this translational approach, and shed new light into the degenerating aspect of MS.

Changes in the manuscript

• Discussion, pag.12: It is important to stress that the aim of this work is not to propose a new animal model of MS, a disease that only affects humans, but rather to validate axonal damage detection (independently from the pathology that has induced it) through noninvasive MRI and apply the framework to characterize axonal pathology in MS.

1.2 I appreciate that both rodent and patient studies are time intensive, major endeavors. Neverthless, the number of subjects is very low in both rodent (n=9) and human (MS=10, control=6) studies. At the very least, this should be more openly acknowledged. But I'm concerned that this is a major weakness of the paper. Related to this, I find it hard to tell how carefully multiple comparison correction was performed throughout. It seems reasonably clear for the TBSS analyses, but then other analyses were performed in ROIs. Are these multiple comparisons corrected as well? Similarly, in Methods, I am confused by the statement that: "post hoc t tests corrected for multiple comparisons whenever a significant effect was detected". What does this mean?

We thank the reviewer for this comment. We agree that a small sample size was a weakness of the previous version of the paper, and therefore, in the new version, we have substantially increased the n for both animal and human experiments (from n=9 to 19 in animals, from 16 to 21 in humans). We removed the ROI analysis in the new version, and thus the confusing statement, and clarified the strategy for multiple comparisons.

Changes in the manuscript

• Data analysis, pag. 18: Lesion masks were excluded from the statistical analysis, and multiple comparisons across clusters were controlled for by using threshold-free cluster enhancement.

1.3 While I do not think the text is in any sense deliberately misleading, I think the authors would do well to either tone down their claims or consider more carefully the implications of the text in many places. Some that stuck out for me are:

Throughout, language in the paper (e.g., "Paired t tests were used to assess differences in the axonal diameter") presumes that the AxCaliber estimates specifically reflect axon diameter. I think the jury is out over whether this is true, particularly for measurements conducted with limited hardware specs. At the very least, I would encourage the author to refer to these measurements throughout as "estimates" of axon diameter.

Thank you for this clarification. We have indeed changed the notation, and now consistently refer to the estimates of axon diameter through MRI as the “MRI axonal diameter proxy”.

1.4 The authors suggest that their results provide "new tools for patient stratification" based on differences in lesion type, but it isn't clear what new information these markers would confer given that the lesions are differentiated based on T1w hypo/hyperintensities. In other words, these lesions are by definition already differentiable from a much simpler MRI marker.

Thank you for this insightful comment. The reviewer is right, and following the general reviewers’ assessment we have decided to not include the lesion analysis in the new version of the manuscript.

1.5 The authors note in the Discussion that: "sensitive to early stages of axonal degeneration, even before alterations in the myelin sheet are detected". Whether intentional or not, the implication in the context of this study is that this would hold for MS (that these markers would detect axonal degeneration preceding demyelination). While there is some discussion of alterations to axonal diameter in MS, the authors do not discuss whether these are the same mechanisms thought to occur in the IBO intervention used here.

Thank you for this comment. Indeed, the scope of the paper is not to assess whether axonal swelling precedes or not myelin alterations, so we agree with the reviewer that this sentence might be misleading and have removed it in the text. While we do not claim that ibotenic acid injections are able to replicate the complex clinical and pathological manifestation of MS (and now we made it clear in the revised manuscript, see comment 1), the electron microscopy paradigm indicates the presence of axonal swelling in the damaged fimbria, which is indeed the same pathological manifestation found in MS post-mortem data (see e.g. Fisher et al. Ann Neurol 2007).

1.6 In the Discussion, the authors note the lack of evidence for a relationship with disability or disease duration, but nevertheless, go on to interpret the "trends" they do observe. I would advise strongly against this: the authors acknowledge that their numbers are low, so I would avoid the temptation to speculate here.

The reviewer is 100% correct. We should have refrained from speculating. In the new version of the paper, however, thanks to the larger human cohort, we were able to find significant associations with disease duration in voxelwise analysis of the white matter skeleton in standard space and in the whole white matter in single subject space (new Figure 5).

1.7 In the Discussion state that "the use of neurofilaments has also been well validated in MS". Well validated for what? MS is a complex disease with a broad range of pathology, so this statement could be read to mean "neurofilaments are known to be altered in MS". However, in the context of this paragraph, the implication would seem to be that neurofilaments are a wellestablished proxy for axonal diameter. Is that the implication, and if so what general evidence is there for this?

We thank the reviewer for this insightful comment. Indeed, altered neurofilaments are not conclusive evidence of increased axonal diameter. In this context, the addition of electron microscopy data in the new manuscript version supports the claim.

Reviewer #2 (Public Review):

Diffusion MRI is sensitive to the brain microstructure, and it has been used to assess the integrity of white matter for nearly 3 decades. Its main limitation is the limited specificity, which makes it difficult to link changes in diffusion parameters to a given pathological substrate. Recently methods based on diffusion MRI that enable the estimation of axonal diameter, non invasively, have become available. This paper aims at validating one of such methods using an experimental model of neurodegeneration. The authors found a significant correlation between axonal diameter estimated by MRI and an histological marker of neurodegeneration. Although this is of great interest, as it demonstrates that this method is sensitive to neurodegeneration, a direct validation would require a measurement of axonal diameter using electron or confocal microscopy, rather than a correlation with a measure of axonal degeneration not directly related to axonal diameter. So, although these data are compelling, they do not prove that the increase in axonal diameter suggested by diffusion MRI corresponds to actual axonal swelling. The Authors also apply the same method to compare the white matter of patients with multiple sclerosis (MS) and healthy controls, showing widespread increases in axonal diameter in the patients. These data are compelling, but again, not conclusive. Other factors such as gloss could bias the MRI measurement and lead to an apparent increase in axonal diameter.

We would like to thank the reviewer for the positive assessment of our work and for the valuable suggestion. We are confident that the new version of the manuscript, by including an extensive validation based on electron microscopy, has addressed the reviewer´s criticisms.

Reviewer #3 (Public Review):

3.1 In this paper, Toschi et al. performed dMRI to in vivo estimate axon diameter in the brain and demonstrated that multi-compartmental modeling (AxCaliber) is sensitive to microstructural axonal damage in rats and axon caliber increase in demyelinating lesions in MS patients, suggesting that axon diameter mapping provides a potential biomarker to bridge the gap between medical imaging contrasts and biological microstructure. In particular, authors injected ibotenic acid (IBO) and saline in the left and right rat hippocampus, respectively, and compared in vivo estimated axon diameter and ex vivo neurofilament staining in left and right fimbria. The axon size estimation was larger in the fimbria of IBO injection side, where the neurofilament intensity is higher. Correlation of axon size estimation and neurofilament intensity was observed in both injection sides. Further, higher axon diameter estimation was observed in normal appearing white matter (NAWM) of MS patients, compared with the healthy subjects. The axon size estimation increased in hypointense lesions of T1 weighted contrast, but not in isointense lesions. Through the comparison of dMRI-estimated axon size and histology-based fluorescence intensity, authors indirectly validated the sensitivity of axon diameter mapping to the tissue microstructure in the rat brain, and further explored the axon size change in the brain of MS patients. However, the dMRI protocol and biophysical modeling in this study were not fully optimized to maximize the sensitivity to axon size estimation, and the dMRI-estimated axon size (4.4-5.4 micron) was much larger than values reported in previous histological studies (0.5-3 micron) [Barazany et al., Brain 2009]. Finally, although the modified AxCaliber model incorporated two fiber bundles in different directions, the fiber dispersion in each bundle was not considered (c.f. fiber dispersion ~20-30 degree in corpus callosum), potentially leading to overestimated axon diameter.

We thank the reviewer for their appreciation of our work, which we believe is substantially improved in this revised version through the inclusion of an electron microscopy paradigm. Below, the point-by-point response to the specific points raised.

3.2 The conclusions in this study are supported by experimental results. However, the dMRI protocol and biophysical model could be further optimized and validated: 1. To in vivo estimate the axon diameter ~1 micron using dMRI, strong diffusion weighting (b-value) should be applied to maximize the signal decay due to intra-axonal restricted diffusion and minimize the signal contribution of extra-cellular hindered diffusion. However, authors only applied maximal b-value = 4000 s/mm2, much smaller than values ~15,00020,000 s/mm2 in previous studies [Assaf et al., MRM 2008; Huang et al., BSAF 2020, 225:1277]. The use of low diffusion weighting in this study leads to a lower bound ~4-6 micron for accurate diameter estimation, the so-called resolution limit in [Nilsson et al., NMR Biomed 2017, 30:e3711]. In other words, the estimated axon diameter is potentially overestimated and related with the imaging protocol and image quality, confounding the biological interpretation.

We thank the reviewer for this insightful comment. Indeed, while the resolution limit is a concern, the chosen b-value has been a compromise between sensitivity to small structure and SNR, as indicated by recent animal (Crater et al., 2022) and human (Jensen et al., 2016; McKinnon et al., 2017; Moss et al., 2019) work, pointing at 3000-4000 s/mm2 as the b-value for which the intra-axonal water signal is dominant. In addition, a paper from the laboratory that first developed the Axcaliber method recently came out (Gast et al., 2023, DOI: 10.1007/s12021-023-09630-w) demonstrating that an MRI protocol with a maximum b-value between 3000 and 4000 s/mm2 (and even lower) is sufficient to capture, in vivo and in humans, various well-known aspects of axonal morphometry (e.g., the corpus callosum axon diameter variation) as well as other aspects that are less explored (e.g., axon diameter-based separation of the superior longitudinal fasciculus into segments). The same paper contains resources and further bibliography supporting the fact that experimental evidence suggests that the contribution of intra-axonal water to restricted diffusion signals dominates other factors (see Online Resource 1, section A of the same paper). To challenge this recent evidence from a neurobiology perspective, we include in the supplementary material a subset of experiments in animals with lower maximum b-value (2500 s/mm2, Fig. S1), where we are able to detect the same effect of increased MRI axonal diameter proxy in the injected hemisphere compared to control.

We would like to add that while extremely valuable and informative, simulation studies such as the excellent study by Veraart et al., 2020, are inevitably valid under certain assumptions. Among them, some critical ones are i) the need to neglect nonaxonal cells such as glia, ii) assuming that the bulk diffusivity of water in cerebral tissue would be the same as that of free water, and iii) impermeable barriers. All these assumptions are expected to play a role in the estimated resolution limit, a role difficult to quantify but likely substantial.

For this reason, we believe that our approach, which is 100% focused on neurobiology and measurements performed in real tissue, can offer a different perspective and fuel the ongoing debate on axonal diameter measurement feasibility. We acknowledge the value of the reviewer comment and discuss the issue of b-value in the discussion (see also comment 1.8).

Changes in the manuscript

• Discussion, pag. 12:<br /> Despite some inevitable minor differences due to different brain sizes and magnet features, the human protocol was built to match the main characteristics of the preclinical diffusion sequence, such as the b-value and diffusion time range. The chosen b-value has been a compromise between sensitivity to small structures and the signalto-noise ratio (SNR), as indicated by recent animal (Crater et al., 2022) and human (Gast et al., 2023; Jensen et al., 2016; McKinnon et al., 2017; Moss et al., 2019) work, pointing at 4000 s/mm2 as the b-value for which the intra-axonal water signal is dominant. However, following recent work supporting sensitivity of diffusion-weighted MRI to axonal diameter even at lower b-values (Gast et al., 2023), we tested a protocol with a lower b-value in a subset of animals, with the aim of facilitating future clinical AxCaliber studies. We found no qualitative differences in the outcome (MRI axonal diameter proxy was increased following fimbria damage). Further work and perhaps more realistic simulations, considering real cell composition and morphology, are needed to clarify this issue.

3.3 In this study, the positive correlation of dMRI-estimated axon size and neurofilament fluorescence intensity is indeed an encouraging result, and yet this validation is indirect since it relies on the positive correlation between neurofilament intensity and axon diameter in histology.

The reviewer correctly points out a severe limitation of the previous manuscript version, which is now addressed by including an extensive electron microscopy evaluation, recapitulated in new Fig. 3.

3.4 Authors did not consider the fiber dispersion in the proposed dMRI model. This can lead to overestimated axon diameter, even in the highly aligned WM, such as corpus callosum with ~20-30 degree dispersion in histology [Ronen et al., BSAF 2014, 219:1773; Leergaard et all, PLoS One 2010, 5(1), e8595] and MRI [Dhital et al., NeuroImage 2019, 189, 543; Novikov et al., NeuroImage 2018, 174:518].

The reviewer is correctly pointing out an important characteristic of while matter microstructure as is fibre dispersion. However, we would like to point out that the use of a second fiber population is expected to mitigate this effect by absorbing some axonal directional dispersion in areas of a single fiber. To support this, we quantified dispersion as the angle between the two main fiber orientations captured by the AxCaliber fit, as showed in Author response image 1 for two representative subjects (one control, upper line, and one MS, lower line; the “dispersion” maps are masked by a white matter probability mask, and superimposed to a T2w). Indeed, the angle between the two main fibres in the corpus callosum is around 20 degrees or lower, compatible with the bibliography cited by the reviewer, and higher in other white matter areas known to be characterized by fiber crossing and dispersion.

Author response image 1.

Angle in radians between the two main fiber orientations captured by the AxCaliber fit, as showed below for two representative subjects (one control, upper line, and one MS, lower line). The dispersion maps are masked by a white matter probability mask (P>=0.95), and superimposed to a T2-weighted image.

Author Response

Reviewer #1 (Public Review):

This paper shows that a principled, interpretable model of auditory stimulus classification can not only capture behavioural data on which the model was trained but somewhat accurately predict behaviour for manipulated stimuli. This is a real achievement and gives an opportunity to use the model to probe potential underlying mechanisms. There are two main weaknesses. Firstly, the task is very simple: distinguishing between just two classes of stimuli. Both model and animals may be using shortcuts to solve the task, for example (this is suggested somewhat by Figure 8 which shows the guinea pig and model can both handle time-reversed stimuli).

The task structure is indeed simple. In the context of categorization tasks that are typically used in animal experiments, however, we would argue that we are the higher end of stimulus complexity. Auditory categories used in most animal experiments typically employ a category boundary along a single stimulus parameter (for example, tone frequency or modulation frequency of AM noise). Only a few recent studies (for example, Yin et al., 2020; Town et al., 2018) have explored animal behavior with “non-compact” stimulus categories. Thus, we consider our task a significant step towards more naturalistic tasks.

We were also faced with the practical factor of the trainability of guinea pigs (GPs). Prior to this study, guinea pigs have been trained using classical conditioning and aversive reinforcement on detecting tone frequency (e.g., Heffner et al., 1971; Edeline et al., 1993). More recently, competitive training paradigms have been developed for appetitive conditioning, using a single “footstep” sound as a target stimulus and manipulated sounds as non-target stimuli (Ojima and Horikawa, 2016). But as GPs had never been trained on more complex tasks before our study, we started with a conservative one vs. one categorization task. We mention this in the Discussion section of the revised manuscript (page 27, line 665).

To determine whether these results hold for more complex tasks as well, after receiving the reviews of the original manuscript, we trained two GPs (that were originally trained and tested on the wheeks vs. whines task) further on a wheeks vs. many (whines, purrs, chuts) task. As earlier, we tested these GPs with new exemplars and verified that they generalized. In the figure below, the average performance of the two GPs on the regular (training) stimuli and novel (generalization) stimuli are shown in gray bars, and individual animal performances are shown as colored discs. The GPs achieved high performance for the novel stimuli, demonstrating generalization. We also implemented a 4-way WTA stage for a wheek vs. many model and verified that the model generalized to new stimuli as well.

For frequency-shifted calls, these two GPs performed better for wheeks vs. many compared to the average for wheeks vs. whines shown in the main manuscript. The 4-way WTA model closely tracked GP behavioral trends.

The psychometric curves for wheeks vs. many categorization in noise (different SNRs) did not differ substantially from the wheeks vs. whines task.

We focused our one vs. many training on the two conditions that showed the greatest modulation in the one vs. one tasks. However, these preliminary results suggest that the one vs. one results presented in the manuscript are likely to extend to more complex classification tasks as well. We chose not to include these new data in the revised manuscript because we performed these experiments on only 2 animals, which were previously trained on a wheeks vs. whines task. In future studies, we plan to directly train animals on one vs. many tasks.

Secondly, the predictions of the model do not appear to be quite as strong as the abstract and text suggest.

We now replace subjective descriptors with actual effect size numbers to avoid overstatingresults. We also include additional modeling (classification based on the long-term spectrum) and discuss alternative possibilities to provide readers with points of comparison. Thus, readers can form their own opinions of the strengths of the observed effects.

The model uses "maximally informative features" found by randomly initialising 1500 possible features and selecting the 20 most informative (in an information-theoretic sense). This is a really interesting approach to take compared to directly optimising some function to maximise performance at a task, or training a deep neural network. It is suggestive of a plausible biological approach and may serve to avoid overfitting the data. In a machine learning sense, it may be acting as a sort of regulariser to avoid overfitting and improve generalisation. The 'features' used are basically spectro-temporal patterns that are matched by sliding a crosscorrelator over the signal and thresholding, which is straightforward and interpretable.

This intuition is indeed accurate – the greedy search algorithm (described in the original visionpaper by Ullman et al., 2002) sequentially adds features that add the most hits and the least false alarms compared to existing members of the MIF set to the final MIF set. The latter criterion (least false alarms) essentially guards against over-fitting for hits alone. A second factor is the intermediate size and complexity of MIFs. When MIFs are too large, there is certainly overfitting to the training exemplars, and the model does not generalize well (Liu et al., 2019).

It is surprising and impressive that the model is able to classify the manipulated stimuli at all. However, I would slightly take issue with the statement that they match behaviour "to a remarkable degree". R^2 values between model and behaviour are 0.444, 0.674, 0.028, 0.011, 0.723, 0.468. For example, in figure 5 the lower R^2 value comes out because the model is not able to use as short segments as the guinea pigs (which the authors comment on in the results and discussion). In figure 6A (speeding up and slowing down the stimuli), the model does worse than the guinea pigs for faster stimuli and better for slower stimuli, which doesn't qualitatively match (not commented on by the authors). The authors state that the poor match is "likely because of random fluctuations in behavior (e..g motivation) across conditions that are unrelated to stimulus parameters" but it's not clear why that would be the case for this experiment and not for others, and there is no evidence shown for it.

Thank you for this feedback. There are two levels at which we addressed these comments inthe revised manuscript.

First, regarding the language – we have now replaced subjective descriptors with the statement that the model captures ~50% of the overall variance in behavioral data. The ~50% number is the average overall R2 between the model and data (0.6 and 0.37 for the chuts vs. purrs and wheeks vs. whine tasks respectively). We leave it to readers to interpret this number.

Second, our original manuscript lacked clarity on exactly what aspects of the categorization behavior we were attempting to model. As recent studies have suggested, categorization behavior can be decomposed into two steps – the acquisition of the knowledge of auditory categories, and the expression of this knowledge in an operant task (Kuchibhotla et al., 2019; Moore and Kuchibhotla, 2022). Our model solely addresses how knowledge regarding categories is acquired (through the detection of maximally informative features). Other than setting a 10% error in our winner-take-all stage, we did not attempt to systematically model any other cognitive-behavioral effects such as the effect of motivation and arousal. Thus, in the revised manuscript, we have included a paragraph at the top of the Results section that defines our intent more clearly (page 5, line 117). We conclude the initial description of the behavior by stating that these factors are not intended to be captured by the model (page 6, line 171). We also edited a paragraph in the Discussion section for clarity on this point (page 26, line 629).

In figure 11, the authors compare the results of training their model with all classes, versus training only with the classes used in the task, and show that with the latter performance is worse and matches the experiment less well. This is a very interesting point, but it could just be the case that there is insufficient training data.

This could indeed be the case, and we acknowledge this as a potential explanation in therevised manuscript (page 22, line 537; page 27, line 653). Our original thinking was that if GPs were also learning discriminative features only using our training exemplars, they would face a similar training data constraint as well. But despite this constraint, the model’s performance is above d’=1 for natural calls – both training and novel calls; it is only the similarity with behavior on the manipulated stimuli that is lower than the one vs. many model. This phenomenon warrants further investigation.

Reviewer #2 (Public Review):

Kar et al aim to further elucidate the main features representing call type categorization in guinea pigs. This paper presents a behavioral paradigm in which 8 guinea pigs (GPs) were trained in a call categorization task between pairs of call types (chuts vs purrs; wheek vs whines). The GPs successfully learned the task and are able to generalize to new exemplars. GPs were tested across pitch-shifted stimuli and stimuli with various temporal manipulations. Complementing this data is multivariate classifier data from a model trained to perform the same task. The classifier model is trained on auditory nerve outputs (not behavioral data) and reaches an accuracy metric comparable to that of the GPs. The authors argue that the model performance is similar to that of the GPs in the manipulated stimuli, therefore, suggesting that the 'mid-level features' that the model uses may be similar to those exploited by the GPs. The behavioral data is impressive: to my knowledge, there is scant previous behavioral data from GPs performing an auditory task beyond audiograms measured using aversive conditioning by Heffner et al., in. 1970. [One exception that is notably omitted from the manuscript is Ojima and Horikawa 2016 (Frontiers)]. Given the popularity of GPs as a model of auditory neurophysiology these data open new avenues for investigation. This paper would be useful for neuroscientists using classifier models to simulate behavioral choice data in similar Go/No-Go experiments, especially in guinea pigs. The significance of the findings rests on the similarity (or not) of the model and GP performance as a validation of the 'intermediary features' approach for categorization. At the moment the study is underpowered for the statistical analysis the authors attempt to employ which frequently relies on non-significant p values for its conclusions; using a more sophisticated approach (a mixed effects model utilizing single trial responses) would provide a more rigorous test of the manipulations on behavior and allow a more complete assessment of the authors' conclusions.

We thank the reviewer for their feedback and the suggestion for a more robust statistical approach. We have now replaced the repeated measures ANOVA based statistics for the behavior and model where more than 2 test conditions were presented (SNR, segment length, tempo shift, and frequency shift) with generalized linear models with a logit link function (logistic activation function). In these models, we predict the trial-by-trial behavioral or model outcome from predictors including stimulus type (Go or Nogo), parameter value (e.g., SNR value), parameter sign (e.g., positive or negative freq. shift), and animal ID as a random effect. To evaluate whether parameter value and sign had a significant contribution to the model, we compare this ‘full’ model against a null model that only has stimulus type as a predictor and animal ID as a random effect. These analyses are described in detail in the Materials and Methods section of the revised manuscript (page 36, line 930).

These analyses reveal significant effects of segment length changes, and weak effects of tempo changes on behavior (as expected by the reviewer). Both the behavior and model showed similar statistical significance (except tempo shift for wheeks vs. whines) for whether performance was significantly affected by a given parameter.

The behavioral data presented here are descriptive. The central conceptual conclusions of the manuscript are derived from the comparison between the model and behavioral data. For these comparisons, the p-value of statistical tests is not used. We realized that a description of how we compared model and behavioral data was not clear in the original manuscript. To compare behavioral data with the model, we fit a line to the d’ values obtained from the model plotted against the d’ values obtained from behavior, and computed the R2 value. We used the mean absolute error (MAE) to quantify the absolute deviation between model and behavior d’ values. Thus, high R2 values would signify a close correspondence between the model and behavior regardless of statistical significance of individual data points. We now clarify this in page 12, line 289. We derive R2 values for individual stimulus manipulations, as well as an overall R2 by pooling across all manipulations (presented in Fig. 11). This is now clarified in page 21, line 494.

Reviewer #3 (Public Review):

The authors designed a behavioral experiment based on a Go/ No-Go paradigm, to train guinea pigs on call categorization. They used two different pairs of call categories: chuts vs. purrs and wheeks vs. whines. During the training of the animals, it turned out that they change their behavioral strategies. Initially, they do not associate the auditory stimuli with rewards, and hence they overweight the No-Go behavior (low hit and false alarm rate). Subsequently, they learned the association between auditory stimuli and reward, leading to overweighting the Go behavior (high hit and false alarm rates). Finally, they learn to discriminate between the two call categories and show the corresponding behaviors, i.e. suppress the Go behavior for No-go stimuli (improved discrimination performance due to stable hit rates but lower false alarm rates).

In order to derive a mechanistic explanation of the observed behaviors, the authors implemented a computational feature-based model, with which they mirrored all animal experiments, and subsequently compared the resulting performances.

Strengths:

In order to construct their model, the authors identified several different sets of so-called MIFs (most informative features) for each call category, that were best suited to accomplish the categorization task. Overall, model performance was in general agreement with behavioral performance for both the chuts vs. purrs and wheeks vs. whines tasks, in a wide range of different scenarios.

Different instances of their model, i.e. models using different of those sets of MIFs, performed equally well. In addition, the authors could show that guinea pigs and models can generalize to categorize new call exemplars very rapidly.

The authors also tested the categorization performance of guinea pigs and models in a more realistic scenario, i.e. communication in noisy environments. They find that both, guinea pigs and the model exhibit similar categorization-in-noise thresholds.

Additionally, the authors also investigated the effect of temporal stretching/compression of calls on categorization performance. Remarkably, this had virtually no negative effect on both, models and animals. And both performed equally well, even for time reversal. Finally, the authors tested the effect of pitch change on categorization performance, and found very similar effects in guinea pigs and models: discrimination performance crucially depends on pitch change, i.e. systematically decreases with the percentage of change.

Weaknesses:

While their computational model can explain certain aspects of call categorization after training, it cannot explain the time course of different behavioral strategies shown by the guinea pigs during learning/training.

Thank you for bringing this up – in hindsight the original manuscript lacked clarity on exactlywhat aspects of the behavior we were trying to model. As recent studies have suggested, categorization behavior can be decomposed into two steps – the acquisition of the knowledge of auditory categories, and the expression of this knowledge in an operant task (Kuchibhotla et al., 2019; Moore and Kuchibhotla, 2022) . Our model solely addresses how knowledge regarding categories is acquired (through the detection of maximally informative features). Other than setting a 10% error in our winner-take-all stage, we did not attempt to systematically model any other cognitive-behavioral effects such as the effect of motivation and arousal, or behavioral strategies. Thus, in the revised manuscript, we have included a paragraph at the top of the Results section that defines our intent more clearly (page 5, line 117). We conclude the initial description of the behavior by stating that these factors are not intended to be captured by the model (page 6, line 171). We also edited a paragraph in the Discussion section for clarity on this point (page 26, line 629).

Furthermore, the model cannot account for the fact that short-duration segments of calls (50ms) already carry sufficient information for call categorization in the guinea pig experiment. Model performance, however, only plateaued after a 200 ms duration, which might be due to the fact that the MIFs were on average about 110 ms long.

The segment-length data indeed demonstrates a deviation between the data and the model.As we had acknowledged in the original manuscript, this observation suggests further constraints (perhaps on feature length and/or bandwidth) that need to be imposed on the model to better match GP behavior. We originally did not perform this analysis because we wanted to demonstrate that a model with minimal assumptions and parameter tuning could capture aspects of GP behavior.

We have now repeated the modeling by constraining the features to a duration of 75 ms (thelowest duration for which GPs show above-threshold performance). We found that the constrained MIF model better matched GP behavior on the segment-length task (R2 of 0.62 and 0.58 for the chuts vs. purrs and wheeks vs. whines tasks; with the model crossing d’=1 for 75 ms segments for most tested cases). The constrained MIF model maintained similarity to behavior for the other manipulations as well, and yielded higher overall R2 values (0.66 for chuts vs. purrs, 0.51 for wheeks vs. whines), thereby explaining an additional 10% of variance in GP behavior.

In the revised manuscript, we included these results (page 28, line 699), and present results from the new analyses as Figure 11 – Figure Supplement 2.

In the temporal stretching/compressing experiment, it remains unclear, if the corresponding MIF kernels used by the models were just stretched/compressed in a temporal direction to compensate for the changed auditory input. If so, the modelling results are trivial. Furthermore, in this case, the model provides no mechanistic explanation of the underlying neural processes. Similarly, in the pitch change experiment, if MIF kernels have been stretched/compressed in the pitch direction, the same drawback applies.

We did not alter the MIFs in any way for the tests – the MIFs were purely derived by trainingthe animal on natural calls. In learning to generalize over the variability in natural calls, the model also achieved the ability to generalize over some manipulated stimuli. The fact that the model tracks GP behavior is a key observation supporting our argument that GPs also learn MIF-like features to accomplish call categorization.

We had mentioned at a few places that the model was only trained on natural calls. To addclarity, we have now included sentences in the time-compression and frequency-shifting results affirming that we did not manipulate the MIFs to match test stimuli. We also include a couple of sentences in the Discussion section’s first paragraph stating the above argument (page 26, line 615).

Author Response

Reviewer #1 (Public Review):

Causality is important and desired but usually difficult to establish. In this work, Park et al. conducted a comprehensive phenome-wide, two-sample Mendelian randomization analysis to infer the casual effects of plasma triglyceride (TG) levels on 2,600 disease traits. They identified causal associations between plasma TG levels and 19 disease traits, related to both atherosclerotic cardiovascular diseases (ASCVD) and non-ASCVD diseases. They used biobank-scale data in both discovery analysis and replication analysis.

The conclusions of this work are mostly supported by the data and analysis, but some aspects need to be clarified and extended.

(1) The datasets used in this study may not be very consistent. For example, UKB participants are aged 40-69 years old at recruitment. In addition, UKB is United Kingdom-based and FinnGen is Finland-based. So the definition of outcomes may not be identical. The authors should discuss the differences between the datasets and their potential effects.

The reviewer is correct about the differences between UKB and FinnGen and that the definition of clinical outcomes between the two datasets may not be identical due to differences in healthcare systems and population demographics. We now mention this in the discussion section as a potential limitation.

Manuscript changes:

Line 520-539: “Third, UKB and FinnGen have innate differences in participant demographics and medical coding systems, due in part to the former being based in the United Kingdom and the latter in Finland. As such, potential misclassification of participants in case-control assignment is a liability to this study. We exercised caution in mapping UKB traits to FinnGen traits, but we were unable to reliably map all “categorical” traits from UKB to corresponding traits in FinnGen, testing for replication only 221 of the 598 associations that were nominally significant in the primary analysis. We note however that, despite geographical differences, both datasets largely involve White European participants of older age, with the mean age in UKB and FinnGen being 56.5 and 59.8, respectively.”

(2) The discovery analysis and replication analysis are not completely independent because data from UKB have been used in both analyses. Although in discovery, the data were used for association with outcomes; while in replication, the data were used for association with exposure. The authors may want to explain if this may cause problems.

The reviewer is correct that UKB data were used in both the discovery and replication analyses with the caveat that the discovery analysis used UKB for outcomes while using GLGC for exposures, whereas the replication analysis used UKB for exposures while using FinnGen for outcomes. We believed this would be a creative use of three different datasets and a strength of the study; however, we agree that examining the implications of this study design is needed to acknowledge potential biases. We now expand on this in the discussion section as a potential limitation.

Manuscript changes:

Lines 539-545: “Fourth, discovery and replication analyses were not completely independent, since UKB data were used in both analyses. This could potentially exacerbate demographic and measurement biases inherent to UKB; however, we show that taking a traditional replication approach using GLGC instead of UKB for selecting exposure instruments in replication returns comparable Tier 1 results (Supplementary Files 5), while losing statistical power to highlight many of the Tier 2 and 3 results.”

(3) As stated in the manuscript, there are three assumptions for MR analysis. The validity of the results depends on the validity of the assumptions. The last two assumptions are usually difficult to validate. To the authors' credit, they conducted sensitivity analyses addressing horizontal pleiotropy, which is related to assumption 3. It would be helpful if the authors can discuss those assumptions explicitly.

We now explicitly state the assumptions of Mendelian randomization in the introduction section and discuss the validity of these assumptions in the discussion section.

Manuscript changes:

Lines 501-514: “The study has several limitations. First, MR is a powerful but potentially fallible method that relies on several key assumptions, namely that genetic instruments are (i) associated with the exposure (the relevance assumption); (ii) have no common cause with the outcome (the independence assumption); and (iii) have effects on the outcome solely through the exposure (the exclusion restriction assumption) (Hartwig et al., 2016). In MR, (i) is relatively straightforward to test, while (ii) and (iii) are difficult to establish unequivocally. As a prominent example, horizontal or type I pleiotropy has been shown to be common in genetic variation, which can bias MR estimates (Verbanck et al., 2018) (Jordan et al., 2019). This occurs when a genetic instrument is associated with multiple traits other than the outcome of interest. To detect and correct for this as best as possible, we used various MR tests as sensitivity analyses that each aim to adjust for or account for the presence of horizontal pleiotropy, including MR-PRESSO, as well as MR-Egger and weighted median methods. There is no universally accepted method that is perfectly robust to horizontal pleiotropy, but we take the best current approach by using multiple methods and examining the consistency of results.”

Reviewer #2 (Public Review):

This work conducted a Mendelian randomization analysis between TG and a large number of disease traits in biobanks. They leverage the publicly available summary statistics from the European samples from the UK Biobank and FinnGen. A solid but routine standard summary-statistics based MR study is conducted. Several significant causal associations from TG to phenotypes are called by setting p-value cutoff with some Bonferroni correction. Sensitivity statistical analyses are conducted which generate largely consistent results. The research problem is important and relevant for public health as well we drug development. Overall this is a solid execution of current methods over appropriate data source and yields a convincing result. The interpretation of the results in discussion is also well-balanced.

While the paper does have strengths in principle, a few technical weaknesses are observed.

They used UK Biobank as the discovery and FinnGen as the replication. But the two cohorts are rather used symmetrically. Especially for the Tier 3 (NB), it seems to be an attempt of reusing the replication cohort as the discovery. I wonder if that would create additional multiple testing burden as a greater number of hypotheses are considered.

We thank the reviewer for this thought-provoking comment. As the reviewer is aware, MR studies have generally not accounted for multiple testing in the past since they have usually focused on single exposures and/or single diseases. Ours is among one of the more unique MR studies taking a phenome-wide, high-throughput approach, so determining the optimal threshold for balancing true-positive vs. false-positive discovery is an important aspect of the study warranting discussion.

We agree that Tier 3 results carry the least stringent level of statistical evidence (i.e., nominally significant in discovery using UK Biobank and Bonferroni-significant in replication using FinnGen), and that these results should be interpreted with caution. As a phenome-wide study, a significant aim of this work was to generate hypotheses, and so, we decided to present our results using the three tiers of statistical evidence to highlight as many promising associations as possible for further investigation. Nevertheless, we now express extra caution in the results and discussion sections regarding Tier 2 and 3 results, and we also note as a limitation that these results especially require external replication.

Manuscript changes:

Lines 438-444: “Regarding non-ASCVDs, we present suggestive genetic evidence of potentially causal associations between plasma TG levels and uterine leiomyomas (uterine fibroids), diverticular disease of intestine, paroxysmal tachycardia, hemorrhage from respiratory passages (hemoptysis), and calculus of kidney and ureter (kidney stones). Due to the weaker statistical evidence supporting these associations, special caution is encouraged when interpreting these results to infer causality, and further replication and validation studies are essential for all Tier 2 and Tier 3 results.”

The replication p-value cutoff is a bit statistically lenient. In a typical discovery-replication setting the two stages are conducted sequentially and replication should go through the Bonferroni adjustment on the number of significant signals from discovery that is tested in the replication. For example, in this case, in tier 2, the cutoff should be 0.05/39. This may make the association of leiomyoma of the uterus slightly non-significant though. Similar cutoff should be applied to tier 3 as well.

We thank the Reviewer for highlighting this important point. We agree that in a standard two-stage discovery and replication study design, the Bonferroni adjustment should be based on the number of significant signals from discovery that is tested in the replication. We had initially considered this approach but chose the current tiered approach based on a number of factors:

First, we had initially considered performing a standard meta-analysis between UK Biobank and FinnGen datasets and using the Bonferroni adjustment of the total number of tests. However, it was not possible to reliably map the phenotypes between UK Biobank and FinnGen on a large-scale due to different classification schemes.

Second, we had noticed that if we only focus on the sequential two-stage design, then we would be ignoring strong causal relationships observed in FinnGen that passed Bonferroni adjustment but may only be nominally associated in UK Biobank. Although not as strong as Tier 1 findings, we believe that these findings warranted some consideration. This is particularly relevant since differences in the strength of the causal relationship could be attributed to the different populations studied, sample size, different health systems used to measure disease outcomes, differences in statistical power in the MR tests between the two stages (e.g., number of IVs), amongst others.

Third, we wanted to point out that the total adjustment for number of phenotypes tested using Bonferroni is a very conservative adjustment because the multiple EHR phenotypes have varying degrees of redundancy and correlation. We believe the appropriate Bonferroni-adjusted P-value cutoff is somewhere in between the Bonferroni adjustment of total number of phenotypes, and the nominal P-value (no adjustment for number of phenotypes).

Although somewhat unconventional, we came up with this tiered P-value approach to overcome the points mentioned above. We have now included text to further explain our approach and to mention that tier 2 and tier 3 results require further replication and validation.

Manuscript changes:

Lines 266-283: “This presentation is somewhat unconventional and partly arises from the study’s use of three different datasets for instrument selection. In a traditional two-stage discovery and replication design, Bonferroni adjustment is based on the number of significant signals from discovery that is tested in replication. Here, we used three tiers of statistical evidence to present results because a standard meta-analysis between UKB and FinnGen was not possible, given it was not possible to reliably map all phenotypes between the two datasets. Additionally, Bonferroni-significant results in the replication analysis would have been ignored in FinnGen in a sequential two-stage design if they were also only nominally associated in UKB. The three tiers are defined below:”

Lines 441-444: “Due to the weaker statistical evidence supporting these associations, special caution is encouraged when interpreting these results to infer causality, and further replication and validation studies are essential for all Tier 2 and Tier 3 results.”

Lines 498-500: “However, we reiterate that this Tier 3 association was only nominally significant in discovery, while Bonferroni-significant in replication, and future studies are needed to validate the statistical evidence.”

Lines 565-567: “However, caution is still warranted in inferring causality, as MR depends on specific assumptions and the validity of those assumptions must be carefully assessed. Thus, diverse study designs remain necessary to triangulate evidence on the causal effects of plasma TG levels.”

The causal effect of TG to leiomyoma of the uterus is weak, as indicated by both the sub-significant in the replication and the non-significant of MR-PRESSO. Similarly, I would recommend more caution on the weak statistical rigor when interpreting Tier 2 and Tier 3 results.

We agree with the Reviewer. We have now emphasized more caution in interpreting Tier 2 and Tier 3 results. We have also explicitly restated the weaker statistical evidence underlying these results and noted need for future validation. Please see our detailed response to the Comment above.

Manuscript changes:

Lines 498-500: “However, we reiterate that this Tier 3 association was only nominally significant in discovery, while Bonferroni-significant in replication, and future studies are needed to validate the statistical evidence.”

Another methodological choice that might need justification is the use of UKB TG GWAS loci (1,248 SNPs) are the instrument for FinnGen. This may create some subtle interference with the use of UKB as outcomes in the discovery analysis. It may be minor but some justification or at least some discussions of potential limitations should be mentioned. What about the alternative of using GLGC as instruments in replication?

We agree with the reviewer that the use of UKB TG GWAS loci (1,248 SNPs) as instruments for FinnGen outcomes needs additional justification. We now detail this decision in the text as copied below.

Additionally, we now present new data comparing MR results on FinnGen outcomes when selecting TG instruments from UKB GWAS versus GLGC GWAS. Statistical significance after Bonferroni correction was set to 0.05/221, where 221 was the number of disease traits nominally significant in UKB that were tested in FinnGen. We note that the results were fairly consistent. All Tier 1 results remained Bonferroni significant, whether using TG SNPs from UKB or GLGC. Though statistical significance decreased for the remaining diseases of interest, the direction of causality remained consistent, and three disease traits remained significant (hypertension, aortic aneurysm, and alcoholic liver disease). These results support that instrumenting TG using 1,248 SNPs from UKB might carry more power than the 141 SNPs from GLGC, allowing for the detection of associations in our initial replication analysis using UKB for exposures and FinnGen for outcomes. We now include this analysis in the text and include the figure below, as well as its underlying data, as supplementals (Supplementary File 5).

Manuscript changes:

Lines 229-236: “We selected UKB TG GWAS loci as the instruments for replication on FinnGen outcomes, rather than GLGC TG GWAS loci, to diversify the source of TG instruments and mitigate potential biases associated with one TG GWAS. Moreover, UKB GWAS included a larger study population than GLGC GWAS, providing a greater number of genetic instruments that can together explain more of the variance in plasma TG levels, and thus, greater statistical power and precision. Nevertheless, we also performed the replication analyses using TG instruments from GLGC and included these results as supplemental data (Supplementary File 5).”

For disease outcomes (line 188), UKB European sample size is ~400,000 rather than ~500,000. Can the author clarify the sample size they used?

We thank the reviewer for catching this detail. We have now clarified the sample size of UKB European participants in the Methods section, and we also included the exact sample size of each disease trait GWAS (cases and controls) in Supplementary Figure 1.

Manuscript changes:

Lines 194-201: “Pan-UKB had performed 16,131 GWASs on 7,221 phenotypes in ~420,531 UKB participants of European ancestry using genetic and phenotypic data (PanUKBTeam, 2020). A total of 7,221 total phenotypes had been categorized as “biomarker”, “continuous”, “categorical”, “ICD-10 code”, “phecode”, or “prescription” (PanUKBTeam, 2020). We filtered for outcomes to retain categorical, ICD-10, and phecode types; non-null heritability in European ancestry as estimated by Pan-UKB; and relevance to disease, excluding medications. This yielded 2,600 traits for primary analysis. The exact sample size of each GWAS for each of these traits is provided in Supplementary File 1.”

It would be reassuring to the reader if the TG measurements were measured in a treatment-naïve manner. GLGC accounted for treatment (at least LDL, check paper for TGs; if they didn’t, there must be reason). Maybe not UKB.

We now provide information about whether the lipid measurements were measured in a treatment-naïve manner in the Methods for GLGC and UKB. We also address this point in the discussion section as a potential limitation.

Manuscript changes:

Lines 179-180: “We note that the GLGC GWAS had excluded individuals known to be on lipid-lowering medications.”

Lines 187-188: “We note that the Pan-UKB GWAS study did not exclude participants based on their use of lipid-lowering medications.”

Lines 545-546: “Fifth, the GLGC GWAS used to select instruments for plasma TG levels in discovery had accounted for lipid-lowering treatment, while the UKB GWAS used in replication had not.”

"Phenome-wide MR is a high-throughput extension of MR that, under specific assumptions, estimates the causal effects of an exposure on multiple outcomes simultaneously." - I guess it is more informative to mention the specific assumptions, at least briefly, in the introduction so it is easier for the reader to interpret the results.

We agree with the reviewer that it would be informative to explicitly state the assumptions of Mendelian randomization. We now explicitly state these assumptions in the introduction.

Manuscript changes:

Lines 123-129: “Phenome-wide MR is a high-throughput extension of MR that estimates the causal effects of an exposure on multiple outcomes simultaneously. As in conventional MR, this method uses genetic variants as instrumental variables (IV) to proxy modifiable exposures (Davey Smith & Ebrahim, 2003), and importantly, it relies on three critical assumptions: (1) The genetic variant is directly associated with the exposure; (2) The genetic variant is unrelated to confounders between the exposure and outcome; and (3) The genetic variant has no effect on the outcome other than through the exposure (Davey Smith & Ebrahim, 2003).”

Reviewer #3 (Public Review):

Park and Bafna et al. applied a genetics-based epidemiological approach, the Mendelian randomization analysis (MR), to evaluate the potential causal roles of triglycerides across 2,600 disease traits (i.e., the phenome). In a typical two-sample MR framework, they utilized existing genome-wide association study (GWAS) summary statistics from two separate studies. They are Global Lipids Genetics Consortium (GLGC) and UK Biobank in the discovery analysis, and UK Biobank and FinnGen in the replication analysis. This replication design is a great strength of the study, enhancing the robustness and reproducibility of the results. For the candidate pairs of causal associations, the authors further perform multiple sensitivity analyses to evaluate the robustness of the results to possible violations of assumptions in MR. To disentangle the independent effects of triglycerides from other lipid fractions (i.e., LDL-cholesterol and HDL-cholesterol), the authors performed multivariable MR analysis. In the end, possible causal associations were revealed in three tiers, based on statistical significance in the two-stage analysis. The results support the causal effects of triglycerides in increasing the risk of atherosclerotic cardiovascular disease. They also reveal novel conditions, which are either new treatable conditions (e.g., leiomyoma, hypertension, calculus of kidney and ureter) for repurposing of triglycerides-lowering drug, or possible side effects (e.g., alcoholic liver disease) the triglyceride-lowering treatment should pay special attention to.

The analysis approaches in the paper are standard and solid. The discovery-replication study design is a great strength. Correction for multiple testing was implemented in a conservative way. The sensitivity analyses and MVMR strengthen the robustness of the results. The manuscript is very clearly written and pleasant to read. The limitations were well-presented. The conclusions and interpretations are mostly supported by the data, with one major concern as explained below. But overall, in addition to the specific findings, this study could be an exemplar study for the use of phenome-wide MR in identifying treatable conditions and side effects for most existing drugs.

1) My major concern is about reverse causation. For example, having atherosclerotic cardiovascular disease increases circulating triglycerides. Reverse causation can induce false positives in MR analysis. With the existing data in this study, the authors can perform a reverse MR to evaluate the effect of the 19 disease traits on triglycerides. Ruling out the presence of reserve causation is important to make sure that the current findings are not false positives.

We agree with the reviewer that performing reverse MR would be important to rule out reverse causation. We now present new results using reverse MR, selecting instruments for disease from UKB and instruments for TG from GLGC (i.e., reversing the discovery analysis). We provide an interpretation of these new results in the discussion section and present the underlying data, including the number of genetic variants used, in Supplementary File 6. Please note we could only perform reverse MR on 9 of the 19 diseases of interest, due to insufficient genetic data in GLGC to extract the specific exposure instruments. As expected, we observed significant associations (orange) between “disorders of lipoprotein metabolism” and “hyperlipidemia” with plasma TG levels; however, all other estimates were non-significant, suggesting unidirectional associations for the remaining seven disease traits. We now include the figure below and its underlying data as supplements (Supplementary File 6).

Manuscript changes:

Lines 258-261 “Finally, we performed bidirectional or reverse MR on significant results to examine the potential presence of reverse causation. We selected instruments for each disease as described above from Pan-UKB and instruments for plasma TG levels from GLGC, essentially reversing the discovery stage design using a fixed-effect IVW method.”

Lines 368-373: “Finally, we performed reverse MR to estimate the effects of significant disease traits on plasma TG levels, selecting instruments from UKB and GLGC, respectively. Genetic data were sufficiently available to perform this analysis for 9 of the 19 diseases of interest. These results are presented in Supplementary File 6. Expectedly, “disorders of lipoprotein metabolism” and “hyperlipidemia” had positive effects on plasma TG levels; however, no other examined disease trait showed results suggesting reverse causation.”

Author Response

Reviewer #1 (Public Review):

The authors have tried to correlate changes in the cellular environment by means of altering temperature, the expression of key cellular factors involved in the viral replication cycle, and small molecules known to affect key viral protein-protein interactions with some physical properties of the liquid condensates of viral origin. The ideas and experiments are extremely interesting as they provide a framework to study viral replication and assembly from a thermodynamic point of view in live cells.

The major strengths of this article are the extremely thoughtful and detailed experimental approach; although this data collection and analysis are most likely extremely time-consuming, the techniques used here are so simple that the main goal and idea of the article become elegant. A second major strength is that in other to understand some of the physicochemical properties of the viral liquid inclusion, they used stimuli that have been very well studied, and thus one can really focus on a relatively easy interpretation of most of the data presented here.

There are three major weaknesses in this article. The way it is written, especially at the beginning, is extremely confusing. First, I would suggest authors should check and review extensively for improvements to the use of English. In particular, the abstract and introduction are extremely hard to understand. Second, in the abstract and introduction, the authors use terms such as "hardening", "perturbing the type/strength of interactions", "stabilization", and "material properties", for just citing some terms. It is clear that the authors do know exactly what they are referring to, but the definitions come so late in the text that it all becomes confusing. The second major weakness is that there is a lack of deep discussion of the physical meaning of some of the measured parameters like "C dense vs inclusion", and "nuclear density and supersaturation". There is a need to explain further the physical consequences of all the graphs. Most of them are discussed in a very superficial manner. The third major weakness is a lack of analysis of phase separations. Some of their data suggest phase transition and/or phase separation, thus, a more in-deep analysis is required. For example, could they calculate the change of entropy and enthalpy of some of these processes? Could they find some boundaries for these transitions between the "hard" (whatever that means) and the liquid?

The authors have achieved almost all their goals, with the caveat of the third weakness I mentioned before. Their work presented in this article is of significant interest and can become extremely important if a more detailed analysis of the thermodynamics parameters is assessed and a better description of the physical phenomenon is provided.

We thank you for the comments and, in particular, for being so positive regarding the strengths of our manuscript and for raising concerns that will surely improve it. We have taken the following actions to address your concerns:

1) Extensive revisions have been made to the use of English, particularly in the abstract and introduction. Key terms are defined as they are introduced in the text to enhance the clarity of the argument. This is a significant revision that is highlighted within the text, but it is too extensive to detail here.

2) In the results section, we improved and extended the discussion of our graphs to the extent possible. However, we found that attempting to explain the graphs' meanings more thoroughly would detract from our manuscript's main focus: identifying thermodynamic changes that could potentially lead to alterations in material properties, specifically aspect ratio, size, and Gibbs free energy. As a result, we introduced the type of information we could obtain from our analyses in the introduction (Lines 112-125) and briefly commented on it in the ‘results’ section (Lines 304-306, sentences below).

From introduction – lines 112-125:

“In addition, other parameters like nucleation density determine how many viral condensates are formed per area of cytosol. Overall, the data will inform us if changing one parameter, e.g. the concentration, drives the system towards larger condensates with the same or more stable properties, or more abundant condensates that are forced to maintain the initial or a different size on account of available nucleation centres (Riback et al., 2020:Snead, 2022 #1152). It will also inform us if liquid viral inclusions behave like a binary or a multi-component system. In a binary mixture, Cdilute is constant (Klosin et al., 2020). However, in multi-component systems, Cdilute increases with bulk concentration (Riback et al., 2020). This type of information could have direct implications about the condensates formed during influenza infection. As the 8 different genomic vRNPs have a similar overall structure, they could, in theory, behave as a binary system between units of vRNPs and Rab11a. However, a change in Cdilute with concentration would mean that the system behaves as a multi-component system. This could raise the hypothesis that the differences in length, RNA sequence and valency that each vRNP has may be relevant for the integrity and behaviour of condensates.”.

From results lines 304-306:

This indicates that the liquid inclusions behave as a multi-component system and allow us to speculate that the differences in length, RNA sequence and valency that each vRNP may be key for the integrity and behaviour of condensates.

3) The reviewer has drawn our attention to the absence of phase separation analysis in our study. We believe that the formation of influenza A virus condensates is governed by phase separation (or percolation coupled to phase separation). However, we must exercise caution at this point because the condensates we are studying are highly complex, and the physics of our cellular system may not be adequate to claim phase separation without being validated by an in vitro reconstitution system. IAV inclusions contain a variety of cellular membranes, different vRNPs, and Rab11a. While we have robust data to propose a model in which the liquid-like properties of IAV inclusions arise from a network of interacting vRNPs that bridge multiple cognate vRNP-Rab11 units on flexible membranes, similar to what occurs in phase-separated vesicles in neurological synapses, our model for this system still lacks formal experimental validation. As a note, the data supporting our model includes: the demonstration of the liquid properties of our liquid inclusions (Alenquer et al. 2019, Nature Communications, 10, 1629); and impairment of recycling endocytic activity during IAV infection Bhagwat et al. 2020, Nat Commun, 11, 23; Kawaguchi et al. 2012, J Virol, 86, 11086-95; Vale-costa et al. 2016, J Cell Sci, 129, 1697-710. This leads to aggregated vesicles seen by correlative light and electron microscopy (Vale-Costa et al., 2016 JCS, 129, 1697-710) and by immunofluorescence and FISH (Amorim et al. 2011,. J Virol 85, 4143-4156; Avilov et al. 2012, Vaccine 30, 7411-7417; Chou et al. 2013, PLoS Pathog 9, e1003358; Eisfeld et al. 2011, J Virol 85, 6117-6126 and Lakdawala et al. 2014, PLoS Pathog 10, e1003971.

To be able to explore the significance of the liquid material properties of IAV inclusions, we used the strategy described in this current work. By developing an effective method to manipulate the material properties of IAV inclusions, we provide evidence that controlled phase transitions can be induced, resulting in decreased vRNP dynamics in cells and a negative impact on progeny virion production. This suggests that the liquid character of liquid inclusions is important for their function in IAV infection. We have improved our explanation addressing this concern in the limitations of our study (as outlined below in the box and in manuscript in lines 857-872).

We are currently establishing an in vitro reconstitution system to formally demonstrate, in an independent publication, that IAV inclusions are formed by phase separation (or percolation coupled to phase separation). For this future work, we teamed up with Pablo Sartori, a theorical physicist to derive in-depth analysis of the thermodynamics of the viral liquid condensates in the in vitro reconstituted system and compare it to results obtained in the cell. This will provide means to establish comparisons. We think that cells have too many variables to derive meaningful physics parameters (such as entropy and enthalpy) and models that need to be complemented by in vitro systems. For example, increasing the concentration inside a cell is not a simple endeavour as it relies on cellular pathways to deliver material to a specific place. At the same time, the 8 vRNPs, as mentioned above, have different size, valency and RNA sequence and can behave very differently in the formation of condensates and maintenance of their material properties. Ideally, they should be analysed individually or in selected combinations. For the future, we will combine data from in vitro reconstitution systems and cells to address this very important point raised by the reviewer.

From the paper on the section ‘Limitations of the study’:

“Understanding condensate biology in living cells is physiological relevant but complex because the systems are heterotypic and away from equilibria. This is especially challenging for influenza A liquid inclusions that are formed by 8 different vRNP complexes, which although sharing the same structure, vary in length, valency, and RNA sequence. In addition, liquid inclusions result from an incompletely understood interactome where vRNPs engage in multiple and distinct intersegment interactions bridging cognate vRNP-Rab11 units on flexible membranes (Chou et al., 2013, Gavazzi et al., 2013, Sugita et al., 2013, Shafiuddin and Boon, 2019, Haralampiev et al., 2020, Le Sage et al., 2020). At present, we lack an in vitro reconstitution system to understand the underlying mechanism governing demixing of vRNP-Rab11a-host membranes from the cytosol. This in vitro system would be useful to explore how the different segments independently modulate the material properties of inclusions, explore if condensates are sites of IAV genome assembly, determine thermodynamic values, thresholds accurately, perform rheological measurements for viscosity and elasticity and validate our findings. The results could be compared to those obtained in cell systems to derive thermodynamic principles happening in a complex system away from equilibrium. Using cells to map how liquid inclusions respond to different perturbations provide the answer of how the system adapts in vivo, but has limitations.

Reviewer #2 (Public Review):

During Influenza virus infection, newly synthesized viral ribonucleoproteins (vRNPs) form cytosolic condensates, postulated as viral genome assembly sites and having liquid properties. vRNP accumulation in liquid viral inclusions requires its association with the cellular protein Rab11a directly via the viral polymerase subunit PB2. Etibor et al. investigate and compare the contributions of entropy, concentration, and valency/strength/type of interactions, on the properties of the vRNP condensates. For this, they subjected infected cells to the following perturbations: temperature variation (4, 37, and 42{degree sign}C), the concentration of viral inclusion drivers (vRNPs and Rab11a), and the number or strength of interactions between vRNPs using nucleozin a well-characterized vRNP sticker. Lowering the temperature (i.e. decreasing the entropic contribution) leads to a mild growth of condensates that does not significantly impact their stability. Altering the concentration of drivers of IAV inclusions impact their size but not their material properties. The most spectacular effect on condensates was observed using nucleozin. The drug dramatically stabilizes vRNP inclusions acting as a condensate hardener. Using a mouse model of influenza infection, the authors provide evidence that the activity of nucleozin is retained in vivo. Finally, using a mass spectrometry approach, they show that the drug affects vRNP solubility in a Rab11a-dependent manner without altering the host proteome profile

The data are compelling and support the idea that drugs that affect the material properties of viral condensates could constitute a new family of antiviral molecules as already described for the respiratory syncytial virus (Risso Ballester et al. Nature. 2021)

Nevertheless, there are some limitations in the study. Several of them are mentioned in a dedicated paragraph at the end of a discussion. This includes the heterogeneity of the system (vRNP of different sizes, interactions between viral and cellular partners far from being understood), which is far from equilibrium, and the absence of minimal in vitro systems that would be useful to further characterize the thermodynamic and the material properties of the condensates.

There are other ones.

We thank reviewer 2 for highlighting specific details that need improving and raising such interesting questions to validate our findings. We have addressed the comments of Reviewer 2, we performed the experiments as described (in blue) below each point raised.

1) The concentrations are mostly evaluated using antibodies. This may be correct for Cdilute. However, measurement of Cdense should be viewed with caution as the antibodies may have some difficulty accessing the inner of the condensates (as already shown in other systems), and this access may depend on some condensate properties (which may evolve along the infection). This might induce artifactual trends in some graphs (as seen in panel 2c), which could, in turn, affect the calculation of some thermodynamic parameters.

The concern of using antibodies to calculate Cdense is valid, and we thought it was very important. We addressed this concern by performing the same analyses using a fluorescent tagged virus that has mNeon Green fused to the viral polymerase PA (PA-mNeonGreen PR8 virus). Like NP, PA is a component of vRNPs and labels viral inclusions, colocalising with Rab11 when vRNPs are in the cytosol. However, per vRNP there is only one molecule of PA, whilst of NP there are 37-96 depending on the size of vRNPs. As predicted, we did observe changes in the Cdilute, Cdense and nucleation density. However, the measurements and values obtained for Gibbs free energy, size, aspect ratio detecting viral inclusions with fluorescently tagged vRNPs or antibody staining followed the same trend and allow us to validate our conclusion that major changes in Gibbs free energy occur solely when there is a change in the valency/strength of interactions but not in temperature or concentration (Figure 1 below). Given the extent of these data, we show here the results but, in the manuscript, we will describe the limitations of using antibodies in our study within the section ‘Limitations of the study’ from lines 881-894. Given the importance of the question regarding the pros and cons of the different systems for analysing thermodynamic parameters, we have decided to systematically assess and explore these differences in detail in a future manuscript.

For more information. This reviewer may be asking why we did not use the PA-fluorescent virus in the first place to evaluate inclusion thermodynamics and avoid problems in accessibility that antibodies may have to get deep into large inclusions. Our answer is that no system is perfect. In the case of the PA-fluorescent virus, the caveats revolve around the fact that the virus is attenuated (Figure 1a below), exhibiting a delayed infection as demonstrated by reduced levels of viral proteins (Figure 1b below). Consistently, it shows differences in the accumulation of vRNPs in the cytosol and viral inclusions form later in infection and the amount of vRNPs in the cytosol does not reach the levels observed in PR8-WT virus. After their emergence, inclusions behave as in the wild-type virus (PR8-WT), fusing and dividing (Figure 1c below) and displaying liquid properties.

As the overarching goal of this manuscript is to evaluate the best strategies to harden liquid IAV inclusions and given that one of the parameters we were testing is concentration, we reasoned that using PR8-WT virus for our analyses would be reasonable.

In conclusions, both systems have caveats that are important to systematically assess, and these differences may shift or alter thermodynamic parameters such as nucleation density, inclusion maturation rate, Cdense, Cdilute in particular by varying the total concentration. As a note, to validate all our results using the PA-mNeonGreen PR8 virus, we considered the delayed kinetics and applied our thermodynamic analyses up to 20 hpi rather than 16 hpi.

However, because of the question raised by this reviewer, on which is the best solution for mitigating errors induced by using antibodies, we re-checked all our data. Not only have we compared the data originated from attenuated fluorescently tagged virus with our data, but also made comparisons with images acquired from Z stacks (as used for concentration and for type/strength of interactions) with those acquired from 2D images. Our analysis revealed that there is a very good match using images acquired with Z-stacks and analysed as Z projections with between antibody staining and vRNP fluorescent virus. Therefore, we re-analysed all our thermodynamic data done with temperature using images acquired from Z stacks and altered entirely Figure 2. We believe that all these comparisons and analyses have greatly improved the manuscript and hence we thank all reviewers for their input.

Figure 1 – The PA-mNeonGreen virus is attenuated in comparison to the WT virus and data obtained is consistent for Gibbs free energy with analyses done with images processed with antibody fluorescent vRNPs. A. Representation of the PA-mNeonGreen virus (PA-mNG; Abbreviations: NCR: non coding region). B. Cells (A549) were transfected with a plasmid encoding mCherry-NP and co-infected with PA-mNeonGreen virus for 16h, at an MOI of 10. Cells were imaged under time-lapse conditions starting at 16 hpi. White boxes highlight vRNPs/viral inclusions in the cytoplasm in the individual frames. The dashed white and yellow lines mark the cell nucleus and the cell periphery, respectively. The yellow arrows indicate the fission/fusion events and movement of vRNPs/ viral inclusions. Bar = 10 µm. Bar in insets = 2 µm. C-D. Cells (A549) were infected or mock-infected with PR8 WT or PA-mNG viruses, at a multiplicity of infection (MOI) of 3, for the indicated times. C. Viral production was determined by plaque assay and plotted as plaque forming units (PFU) per milliliter (mL) ± standard error of the mean (SEM). Data are a pool from 2 independent experiments. D. The levels of viral PA, NP and M2 proteins and actin in cell lysates at the indicated time points were determined by western blotting. (E-G) Biophysical calculations in cells infected with the PA-mNeonGreen virus upon altering temperature (at 10 hpi, evaluating the concentration of vRNPs (over a time course) in conditions expressing native amounts of Rab11a or overexpressing low levels of Rab11a and upon altering the type/strength of vRNP interactions by adding nucleozin at 10 hpi during the indicated time periods. All data: Ccytoplasm/Cnucleus; Cdense, Cdilute, area aspect ratio and Gibbs free energy are represented as boxplots. Above each boxplot, same letters indicate no significant difference between them, while different letters indicate a statistical significance at α = 0.05 using one-way ANOVA, followed by Tukey multiple comparisons of means for parametric analysis, or Kruskal-Wallis Bonferroni treatment for non-parametric analysis.

2) Although the authors have demonstrated that vRNP condensates exhibit several key characteristics of liquid condensates (they fuse and divide, they dissolve upon hypotonic shock or upon incubation with 1,6-hexanediol, FRAP experiments are consistent with a liquid nature), their aspect ratio (with a median above 1.4) is much higher than the aspect ratio observed for other cellular or viral liquid compartments. This is intriguing and might be discussed.

IAV inclusions have been shown to interact with microtubules and the endoplasmic reticulum, that confers movement, and undergo fusion and fission events. We propose that these interactions and movement impose strength and deform inclusions making them less spherical. To validate this assumption, we compared the aspect ratio of viral inclusions in the absence and presence of nocodazole (that abrogates microtubule-based movement). The data in figure 2 shows that in the presence of nocodazole, the aspect ratio decreases from 1.42±0.36 to 1.26 ±0.17, supporting our assumption.

Figure 2 – Treatment with nocodazole reduces the aspect ratio of influenza A virus inclusions. Cells (A549) were infected with PR8 WT for 8 h and treated with nocodazole (10 µg/mL) for 2h, after which the movement of influenza A virus inclusions was captured by live cell imaging. Viral inclusions were segmented, and the aspect ratio measured by imageJ, analysed and plotted in R.

3) Similarly, the fusion event presented at the bottom of figure 3I is dubious. It might as well be an aggregation of condensates without fusion.

We have changed this (check Fig 5A and B in the manuscript), thank you for the suggestion.

4) The authors could have more systematically performed FRAP/FLAPh experiments on cells expressing fluorescent versions of both NP and Rab11a to investigate the influence of condensate size, time after infection, or global concentrations of Rab11a in the cell (using the total fluorescence of overexpressed GFP-Rab11a as a proxy) on condensate properties.

We have included a new figure, figure 5 with the suggested data.

Author Response

Reviewer #1 (Public Review):

This paper evaluates the effect of knocking out CST7(Cystatin 5) on the APPNL-G-F Alzheimer's disease mouse model. They found sexually dimorphic outcomes, with differential transcriptional responses, increased phagocytosis (but interestingly a higher plaque burden) in females and suppressed inflammatory microglial activation in males (but interestingly no change in plaque burden). This study offers new insight into the functional role of CST7 that is upregulated in a subset of disease- associated microglia in AD models and human brain. Despite the discovery of disease-associated microglia several years ago, there has been little effort in understanding the function of the different genes that make up this profile, making this paper especially timely. Overall, the experiments are well-controlled and the data support the main conclusions and the manuscript could be strengthened by addressing the below comments and clarifying questions that could impact the interpretation of their data/ findings.

1) In the first section discussing CST7 expression levels in AD models, it would be good to involve a discussion of levels of CST7 change in human AD samples. There are sufficient available datasets to look at this, and it would help us understand how comparable the animal models are to human patients. For example, while in mice CST7 is highly enriched in microglia/macrophages, in human datasets it seems like it is not quite so specific to microglia - it is equally expressed in endothelial cells. This might have a significant impact on the interpretation of the data, and it would be good to introduce and assess the findings in mice through the human subjects lens. There is a discussion of the human data in the discussion section, but it would be more appropriately assessed in the same way as the mouse data and comparatively presented in the results section. The authors could also include the data from Gerrits et al. 2021 in their first figure.

We agree with the reviewer on the importance of considering the work in the context of human disease. While CST7 is not as strongly upregulated in human AD brain as it is in mouse expression is observed predominantly in myeloid cells in the brain with very minimal expression detected in endothelial cells (see screenshots in Author response image 1 from Brain Myeloid Landscape platform (http://research-pub.gene.com/BrainMyeloidLandscape/BrainMyeloidLandscape2/) and is enriched in AD clusters vs homeostatic in scRNASeq studies (Gerrits et al., 2021). We attempted immunostaining for human CF (CST7) in AD brains to assess expression and co-localisation with microglial markers but failed to validate any of the antibodies tested. Additionally, King et al., 2023 (PMID: 36547260) recently showed increase in CST7 expression in bulk hippocampal RNASeq in AD vs mid-life controls suggesting an ageing/AD mechanism. CST7 has also been shown to be expressed following overexpression of TREM2 in human microglia in vitro and that siRNA-mediated knockdown of expression leads to an increase in phagocytosis (Popescu et al., 2023 - PMID: 36480007), mirroring our data and suggesting a conserved role in human cells. Overall, we believe that, even in the context of mouse models, the understanding of the function of genes upregulated in disease is of importance to the field and that this study paves the way for further work investigating human CST7 in disease. We have added this (with citations to the datasets mentioned) to the discussion (highlighted).

Author response image 1

2) The differential RNAseq data is perhaps one of the most striking results of this paper; however it is difficult to see exactly how similar the male v female APPNL-G-F profiles are, in addition to the genes shared or not between the KO condition. Venn diagrams, in addition to statistical tests, would enhance this part of the paper and add more clarity.

We have added Venn diagrams to show DEGs between male and female AppNL-G-F microglia vs WT control to show how similar the male v female APPNL-G-F profiles are. Additionally, to exemplify the Cst7KO-Sex interaction, a Venn showing DEGs between male and female AppNL-G-F microglia vs. AppNL-G-FCst7-/- microglia (Fig. 2 – Fig. supplement 3). We confirm we have derived all differential gene expression changes reported (including those represented in the Venn diagrams) using appropriate Padj statistical approaches (see Methods).

3) A major argument in the paper is a continuation of Sala-Frigerio 2019 which says that the female phenotype is an acceleration of the male phenotype. Does this mean that if males were assessed at later timepoints, they would be more similar to the females? Or are there intrinsic differences that never resolve? It would be helpful to see a later timepoint for males to get at the difference between these two options

This is an interesting question and while we acknowledge that empirically addressing with a later timepoint could add insight, we believe it would actually need multiple closely-spaced timepoints as choosing what single later timepoint would be optimal is difficult to judge (and likely not possible at all) for reasons below. We also believe data already published combined with our observations show it is most-likely a cell-intrinsic effect that explains our sex-specific differences.

First, we emphasize the acceleration of the microglial phenotype in female AppNL-G-F mice previously published is fairly subtle and relative rather than absolute e.g. the DAM/ARM microglia state represents ~50% of all microglia in male and ~55% of all microglia in females at 12 months old therefore both sexes have similarly abundant microglia in the state that most highly express Cst7. Indeed, after the age at which DAM/ARM state microglia appear in appreciable numbers (~ 6 months), both females and males both have an abundance of them. It is important to note that a 12-month male is far more “progressed” than a 6-month female hence the stepped age effect is temporally short.

Second, Cst7 deletion in the AppNL-G-F mice condition caused qualitative differences affecting distinct genes and/or overlapping genes moving in different directions between female and male mice - if a stepped age effect explained sex differences from Cst7 deletion, given that it could only be stepped by a very short timeframe (several weeks maximum) from reasoning above, we would expect to see similar qualitative changes but of different magnitude in female and male mice arising from Cst7 deletion; this is not the pattern we see.

Third, beyond 12 months old, regression from ARM/DAM actually occurs, again making it unlikely males would “catch up” with females to show the same profile from Cst7 deletion but just at an older age – practically, this also complicates choosing a single later timepoint (and age-related systemic morbidity emerges as a potential confounder as well).

In summary, while the acceleration of the DAM signature in female microglia offers an intriguing possible explanation to our observation of sexual dimorphism in response to deletion of one of the key genes in this signature, we believe it more likely that intrinsic effects are responsible for the Cst7 deletion sex-related impact. Taking the alternative perspective, even if a stepped age effect in the underlying progression of the model could explain our findings, this would need multiple timepoints with short gaps between (e.g. monthly at 12, 13, 14, 15 months old) to provide the temporal resolution to expose this pattern; we would not have the resources to conduct such a resource-intensive and lengthy study. We hope this reasoning appears logical and conscious of the importance to convey this in our manuscript we have revised the Discussion to as concisely as possible capture some key points outlined above.

4) If the central argument is that CST7 in females decreases phagocytosis and in males increases microglia activation, are there changes in amyloid plaque burden or structure in the APPNL-G-F /CST 7 KO mice compared to APPNL-G-F/CST7 WT that reflect these changes? Please address. If not, how does this affect the functional interpretation of differential expression observed in phagocytic/reactive microglia genes? Pieces of this are discussed but it could be clearer.

We emphasise the data already presented in Fig 6 and Fig. 6 – Fig. Supplement 2 showing altered Aβ burden (6E10 staining) and plaque count (MeX04) but no change in plaque area. Regarding the functional interpretation of Cst7-dependent gene changes in microglia beyond the endolysosomal function we present in figures 3-5, we have included additional data using simple immunohistochemistry, as suggested by the reviewer, to assess synapse abundance. We show loss of Sy38 coverage around plaques (Fig. 6I) and a moderate but significant decrease in coverage between AppNL-G-F/Cst7-/- vs AppNL-G-F brains only in females (Fig. 6J). This reflects the effect observed with plaque coverage whereby we observe increased burden in AppNL-G-F/Cst7-/- vs AppNL-G-F females but not males (Fig. 6B-F) suggesting the increased plaque burden in Cst7-/- female mice may lead to increased synapse loss. We would also emphasise that altered expression of phagolysosomal genes could affect disease in ways beyond interactions with amyloid and synapses.

5) It is confusing that increased phagocytosis in the APPNL-G-F/CST7 KO females leads to greater plaque burden, considering proteolysis is not affected. What might explain this observation? Additionally, it is interesting that suppression of microglial activation doesn't lead to an increase in plaques in the male APPNL-G-F/CST7 KO mice. How does the profile of phagocytic microglia in the male APPNL-G-F/CST7 KO mice differ from the APPNL-G-F males?

We emphasize our comments on this topic in the discussion where we speculate that the greater plaque burden in females is linked to increased uptake of Aβ (which we observe in Fig. 4B&C) and deposition into plaques as suggested by Huang et al., 2021 (PMID: 33859405), d’Errico et al., 2022 (PMID: 34811521) and Shabestari et al., 2022 (PMID: 35705056). Regarding the lack of effect in males despite the suppression of inflammatory genes, we agree this is a curious observation, although may point to as yet ill-defined mechanisms for how inflammatory pathways influence plaque pathology. Unfortunately, we were not able to specifically compare the profile of phagocytic microglia in AppNL-G-F vs AppNL-G-FCst7-/- as we did not perform single-cell RNASeq. However, our bulk RNASeq profiling suggests modest downregulation of phagocytic/endolysosomal genes (eg Lilrb4a, Fig. 2I) and reduced expression of LAMP2 in microglia by immunostaining. We have added further comment on this in the discussion.

6) Seems that the authors have potentially discovered an unusual mechanism for how CST7 could regulate cell autonomous function without impacting its canonical protease target. The authors deal with this extensively in the discussion but an ELISA or ICC to localize CST7 to microglia in vitro or in vitro would help address this point.

We have added FISH data localising Cst7 expression to IBA1+ cells specifically around plaques in App brains (Fig. 1B-E). We agree that assessing the subcellular localisation and any non-microglial expression of Cystatin-F (the protein coded by Cst7) would offer valuable insight into the protease target and may reveal details on the precise mechanism by which CF deletion leads the phenotype we observe in this study. However, despite attempting numerous commercially available and gifted antibodies to detect CF we were unable to validate (using Cst7-/- as controls) any methods other than FISH.

7) The authors focus on plaques in their final figure, however dysregulated microglial phagocytosis could impact many other aspects of brain health. Simple immunohistochemistry for synapses and myelin/oligodendrocytes (especially given the results of the in vitro phagocytosis assay) could provide more insight here.

We fully agree with the reviewer. As also outlined in our responses elsewhere, phagocytic changes could have multiple consequences, and we have included additional data using immunohistochemistry as advised for synapses in WT, AppNL-G-F, and AppNL-G-F/Cst7-/- brains. We show loss of Sy38 coverage around plaques (Fig. 6I) and a moderate but significant decrease in coverage between AppNL-G-F/Cst7-/- vs AppNL-G-F brains only in females (Fig. 6J). This reflects the effect observed with plaque coverage whereby we observe increased burden in AppNL-G-F/Cst7-/- vs AppNL-G-F females but not males (Fig. 6B-F) suggesting the increased plaque burden in Cst7-/- female mice may lead to increased synapse loss.

We also performed immunohistochemistry for myelin makers MAG and MBP but found no plaque-associated pathology. Finally, we searched for dystrophic neurites using LAMP1 but found that the antibody stained microglial lysosomes rather than dystrophic neurites in this model (see Author response image 2), an observation that has been made by others (Sharoar et al., 2021 - PMID: 34215298).

Overall, our data suggest Cst7 may play a protective role in females, limiting phagocytosis, reducing plaque burden and blunting synapse loss.

Author response image 2.

Reviewer #3 (Public Review):

In this manuscript, Daniels et al explored the role of Cystatin F in an A-driven mouse model of Alzheimer's disease. By crossing a constitutive knockout mouse lacking the gene that encodes Cystatin F, Cst7, to the AppNL-G-F mouse line, the authors describe impairments in microglial gene expression and phagocytic function that emerge more prominently in females versus males lacking Cst7. A strength of the study is its focus: given mounting evidence that microglia are a hub of neurological dysfunction with particular potential to trigger or exacerbate neurodegenerative disorders, it is essential to determine the changes in microglia that occur pathologically to promote disease progression. Similarly, the wide-spread identification of the gene in question, Cst7, as upregulated in AD models makes this gene a good target for mechanistic studies.

The paper in its current form also has several weaknesses which limit the insights derived, weaknesses that are largely related to the experimental tools and approaches chosen by the authors to test their hypotheses. For example, the paper begins with a figure replotting data from previous studies showing that Cst7 is upregulated in mouse models of Alzheimer's disease. Though relevant to the current study, there are no new insights provided here. Next, the authors perform bulk RNA-sequencing on microglia isolated from male and female mice in the Cst7-/-; AppNL-G-F mouse line. In the methods, it is unclear whether the authors took precautions to preserve the endogenous transcriptional state of these cells given evidence that microglia can acquire a DAM-like signature simply due to the process of dissociation (Marsh et al, Nature Neuroscience, 2022). If the authors did not control for this, their results may not support the conclusions they draw from the data. Relatedly, it appears the authors pooled all microglia together here, instead of just isolating DAMs specifically or analyzing microglia at single-cell resolution, which could reveal the heterogeneous nature of the role of Cst7 in microglia. In addition to losing information about heterogeneity, another concern is that they could be diluting out the major effects of the model on microglial function by including all microglia. Overall, the biggest issue I have with the RNA-sequencing data is the lack of validation of the gene expression changes identified using a different method that does not require dissociation, like immunohistochemistry or fluorescence in situ hybridization. Especially given the limited number of genes they found to be mis-regulated (see Fig. 2 E and G), I worry that these changes might simply be noise, especially since the authors provide no further evidence of their mis-regulation. Without further validation, the data presented are not sufficient to support the authors' claims.

We believe we have addressed this comment in the “Essential Revisions (for the authors)” section above. Please see again below:

We took standard precautions to minimise the risk of aberrant ex vivo cell activation, including maintaining cells on ice during non-enzyme steps of the procedure and carrying out preps in small batches to minimise time taken from removal of brain to purification of microglial RNA. Importantly, we also validated key expression data by in situ methods such as RNA FISH for Cst7 and Lilrb4a (Fig. 1B-E, Fig 2. - Fig. supplement 3) thus eliminating dissection-induced effects. Additionally, when performing qPCR on microglia from non-disease mice to test the disease-specific role of Cst7-dependent gene regulation we did not observe the same gene changes (Fig 2. - Fig. supplement 4) which, if such changes were dependent on tissue dissociation, we would expect to observe in WT or disease animals. We utilised the resources provided by Marsh et al. 2022 to search for overlap between enzyme-induced genes and our DEG lists from our key comparisons. We found the enzyme-induced gene set had very minimal overlap with any of our comparisons with overlap of only 4 genes between enzyme-induced genes and Cst7-dependent genes in males and no overlap between enzyme-induced genes and Cst7-dependent genes in females. We would further point out that the disease-induced microglial RNAseq profile in the AppNL-G-F Cst7+/+ (i.e. disease WT) condition mirrors those observed previously by multiple methods including in situ profiling (Zeng et al 2023 - PMID: 36732642) and RiboTag approaches (Kang et al 2018 - PMID: 30082275). We believe these combined approaches provide convincing validation of the RNAseq data.

In assessing the changes in microglial function and A pathology that occur in males and females of the Cst7-/-; AppNL-G-F line, the authors identify some differences between how females and males are affected by the loss of Cst7. While the statistical analyses the authors perform as given in the figure legends appear to be correct, the plots do not show significant changes between males and females for a given parameter. Take for example Figure 3H. Loss of Cst7 decreases IBA+Lamp+ microglia in males but increases this parameter in females. However, it does not appear that there is a significant difference in IBA+Lamp+ microglia in male versus female mice lacking Cst7. If there is no absolute difference between males and females, can the differential effects of Cst7 knockout on the sexes really be so relevant to the sexual dimorphism observed in the disease? I question this connection, but perhaps a greater discussion of what the result might mean by the authors would be helpful for placing this into context.

We understand the reviewer’s perspective and we agree that the interpretations could be presented and explained better in the text - we have updated the discussion as suggested to address this.

We designed our study initially to search for sex-specific effects of Cst7. Therefore, whilst our ANOVA does include main effects analysis for disease or sex, we carried out post-hoc analysis primarily to investigate effects of Cst7 deletion within sex. In the case of Fig. 3H pointed out by the reviewer, we observe a main effect for disease in the ANOVA and for disease-sex interaction but not for sex. Post-hoc analysis revealed the sex-specific effects of Cst7 we describe in the manuscript. This approach on analysis was also taken by Hoghooghi et al. (2020 - PMID: 33027652) who show related pathway gene Cstc is detrimental in EAE in females but not males (included in the discussion in this manuscript). The observation in Fig. 3H that there appears to be a Cst7 effect in males and females but not a sex effect in Cst7-/- is accurate but a relative anomaly in this study. Generally, we find that, alongside Cst7 deletion affecting females differently to males, we also see a sex effect in Cst7-/- animals but not in Cst7+/+ animals i.e. absolute levels in disease condition as well as relative changes from control to disease condition are different between males and females. This is exemplified in Fig. 4B&C where we observe increased microglial Aβ in female Cst7-/- animals vs male Cst7-/- animals and in Fig. 6D where we observe increased Aβ plaque burden in female Cst7-/- animals vs male Cst7-/- animals. This is most strikingly demonstrated in the case of our RNASeq data where we observe a difference in sex-dependent genes in AppNL-G-F vs AppNL-G-F/Cst7-/- (Fig. 2 – Fig. supplement 3B) implying removal of the Cst7 gene led to an ‘unlocking’ of sexual dimorphism in our cohort which we comment on in the discussion.

Finally, the use of in vitro assays of microglial function can be helpful as secondary analyses when coupled with in vivo or ex vivo approaches, but are not on their own sufficient to support the authors' conclusions. Quantitative engulfment assays (see Schafer et al, Neuron, 2012) on brain tissue showing that male and female microglia lacking Cst7 engulf different amounts of material (e.g. plaques, synapses, myelin) in the intact brain would be more convincing.

We agree that in vitro assays for microglial function are not always sufficient as standalone methods to support conclusions on functions in disease. The reviewer may have missed our in vivo MeX04 uptake assays (Fig 4A-D) which use measurements by flow cytometry on isolated microglia, this is a reflection of the microglial uptake in vivo following MeX04 injection pre-mortem – this experiment showed increased microglial Aβ in female Cst7-/- animals vs male Cst7-/- animals (Fig. 4B&C). Our in vitro assays complement and extend insight in ways not possible in vivo, for example they offer key insight into uptake/degradation kinetics that would be extremely challenging to carry out in vivo.

In general, a major limitation to the insights that can be derived in the study is the decision of the authors to perform all experiments at a single late-stage time point of 12 months of age. As this is quite far into disease progression for many AD models, phenotypic changes identified by the authors could arise due to the downstream effects of plaque deposition and therefore may not implicate Cst7 as a mechanism driving neurodegeneration rather than one of many inflammatory changes that accompany AD mouse models nearing the one-year time point. A related problem is that the study uses a constitutive KO mouse that has lacked Cst7 expression throughout life, not just during disease processes that increase with aging. In summary, the topic of the article is important and timely, but the connection between the data and the authors' conclusions is not as strong as it could be.

As described above, Cst7 expression is absent at steady-state and low until 6-12 months. Therefore, we predict that deletion would have little effect until 12+ months whereby cells expressing Cst7 have had the temporal window to affect disease pathology, as we find in the current study. This was a key part of the reasoning in our choice of the 12-month age for analyses. The negligible expression of Cst7 at baseline/early stages of disease suggests constitutive KO of the gene will not impact the phenotype until disease onset. This is substantiated by the lack of any genotype-related differences in the WT vs Cst7-/- comparisons in the non-disease condition.

Author Response

Reviewer #2 (Public Review):

In this manuscript, the authors performed single-cell RNA sequencing (scRNA-seq) analysis on bone marrow CD34+ cells from young and old healthy donors to understand the age-dependent cellular and molecular alterations during human hematopoiesis. Using a logistic regression classifier trained on young healthy donors, they identified cell-type composition changes in old donors, including an expansion of hematopoietic stem cells (HSCs) and a reduction of committed lymphoid and myeloid lineages. They also identified cell-type-specific molecular alterations between young and old donors and age-associated changes in differentiation trajectories and gene regulatory networks (GRNs). Furthermore, by comparing the single-cell atlas of normal hematopoiesis with that of myelodysplastic syndrome (MDS), they characterized cellular and molecular perturbations affecting normal hematopoiesis in MDS.

The present manuscript provides a valuable single-cell transcriptomic resource to understand normal hematopoiesis in humans and the age-dependent cellular and molecular alterations. However, their main claims are not well supported by the data presented. All results were based on computational predictions, not experimentally validated.

Major points:

1) The authors constructed a regularized logistic regression trained on young donors with manually annotated cell types and predicted cell type labels of cells from old and MDS samples. As the manual annotation of cell types was implicitly assumed as ground truth in this manuscript, I'm wondering whether the predicted cell types in old and MDS samples are consistent with the manual annotation. They should apply the same strategy used in young samples for manual annotation to old and MDS samples, and evaluate how accurate their classifier is.

We performed manual annotation for each MDS sample independently, and for the 3 healthy elderly donors integrated dataset. To do so, we performed unsupervised clustering with Seurat and annotated the clusters using the same set of canonical marker genes that we used for the young data. We then analyzed the correspondences between the annotated clusters and the predictions by GLMnet. Results are shown on Figure 1a. We observe that the biggest disagreements between methods occur between adjacent identities, such as HSC and LMPP, GMP and GMP with more prominent granulocytes profile, or MEP, early and late erythroid. When we explore these disagreements along the erythroid branch, we see that they particularly occur close to the border between subpopulations (Figure 1b). This is consistent with the continuous nature of the differentiation and the difficulty to establish boundaries between cell compartments. However, we observe that miss-labeling between different hematopoietic lineages is rare.

In addition, unsupervised clustering was not always able to directly separate the data in the expected subpopulations. We can see different clusters containing the same cell types (e.g. LMPP1, LMPP2), as well as individual clusters containing cells with different identities (e.g. pDC and monocyte progenitors). This is usually due to sources of variability different to cell identity present in the data Additional, supervised finetuning by local sub clustering and merging would be needed to correct for this. On the contrary, we believe that our GLMnet-based method focusses on gene expression related to identity, resulting in a classification that is better suited for our purpose.

Figure 1 Comparison between GLMnet predictions and manually annotated clusters A) Heatmaps showing percentages of cells in manually annotated clusters (columns) that have been assigned to each of the cell identities predicted by our GLMnet classification method (rows). The analysis was performed independently for the elderly integrated dataset and for every MDS sample. B) UMAP plots showing disagreements in classification between adjacent cell compartments in the erythroid branch. Cells from one erythroid cluster per patient are colored by the identity assigned by the GLMnet classifier. Cells in gray are not in the highlighted cluster, nor labeled as MEP, erythroid early or erythroid late by our classifier.

2) The cell-type composition changes in Figures 1 and 4 were descriptively presented without providing the statistical significance of the changes. In addition, the age-dependent cell-type composition changes should be validated by flow cytometry.

We thank the reviewer for the comment. Significance of the changes is included in Supplementary File 3. In addition, we included the percentage of several cell types we validated by flow cytometry, namely HSCs, GMPs and MEPs, in young and elderly healthy individuals in the manuscript, as Figure 1-figure supplement 3. Similarly to what we detected in our bioinformatic analyses, flow cytometry data demonstrated a significant increase in the percentage of HSCs, as well as an increasing trend in MEPs and a slight decrease in the percentage of GMPs in elderly individuals, corroborating our previous results.

3) In Figure 2, the authors used two different pseudo-time inference methods, STREAM, and Palantir. It is not clear why they used two different methods for trajectory inference. Do they provide the same differentiation trajectories? How robust are the results of trajectory inference algorithms? It seems to be inconsistent that the pseudotime inferred by STREAM was not used for downstream analysis and the new pseudotime was recalculated by using Palantir.

We thank the reviewer for the comment. The reason behind using two different methods to perform similar analyses, is that each of them provides specific outputs that can be used to perform a more robust and comprehensive analysis. STREAM allows to unravel the differentiation trajectories in a single cell dataset with an unsupervised approach. Also the visualization provided by STREAM (Figure 2C and 2D) allows for a simple interpretation of the results to the reader. On the other hand, Palantir provides a more robust analysis to dissect how gene expression dynamics interact and change with differentiation trajectories. For this reason, we decided to use this second method to investigate how specific genes were altered in the monocytic compartment.

As a resource article, the showcase of different methods can be valuable as it provides examples on how each tool can be used to obtain specific results, which can help any reader to decide which might be the best tool for their specific case.

Just to confirm that pseudotime results are similar, we perform a correlation analysis with the pseudotime values obtained from each method. We observed a correlation coefficient of 0.78 (p.val < 2.2e-16) confirming the similarity among both tools.

Figure 2. Correlation analysis of pseudotime values obtained with STREAM and PALANTIR.

4) In Figure 2D, some HSCs seem to be committed to the erythroid lineage. The authors should carefully examine whether these HSCs are genuinely HSCS, not early erythroid progenitors.

We thank the reviewer for the comment. We have performed a deep analysis regarding the classification of HSCs (See Figure 3). Our analyses reveal that none of the cells classified as HSCs express early erythroid progenitor markers. We have also used STREAM to show the expression of these markers along the obtained trajectory and observed that erythroid markers show expression in the erythroid trajectory but not in the HSC compartment (Figure 4).

Figure 3 Expression of marker genes in the HSC compartment. Dot plot depicting the normalized scaled expression of canonical marker genes by HSC of the 5 young and 3 elderly healthy donors. Marker genes are colored by the cell population they characterize. Dot color represents expression levels, and dot size represents the percentage of cells that express a gene.

Figure 4. Expression of erythroid markers in STREAM trajectories. Expression of GATA1 and HBB (erythroid markers) in the predicted differentiation trajectories.

5) It is not clear how the authors draw a conclusion from Figure 3D that the number of common targets between transcription factors is reduced. Some quantifications should be provided.

We thank the reviewer for the comment. We have updated the manuscript to better reflect our findings and emphasize that the predicted regulatory networks of HSCs in elderly donors is displayed as an independent network, compared to the young donors. (Page 6, line 36).

“Overall, we observed that the predicted regulatory network of elderly HSCs (Figure 3d) appeared as an independent network compared to the young GRN. This finding could result in the loss of co-regulatory mechanisms in the elderly donors.”

6) The constructed GRNs and related descriptions were based solely on the SCENIC analysis. By providing the results of an orthogonal prediction method for GRNs, the authors should evaluate how robust and consistent their predictions are.

We thank the reviewer for the comment regarding the method to build gene regulatory networks. As a resource article, our manuscript describes a complete workflow to perform different aspects of single cell analyses. These steps go from automated classification, trajectory inference and GRN prediction. All the selected algorithms have already been benchmarked and compared against other tools that perform similar analysis. SCENIC has already been benchmarked against other algorithms (11) and by others (12).

We do agree with the reviewer that these new predictions could provide strength to our findings, however we believe that these orthogonal predictions would better fit if our article was intended for the Research Article category instead of Tools and Resources.

7) The observed age-dependent cellular and molecular alterations in human hematopoiesis are interesting, but I'm wondering whether the observed alterations are driven by inflammatory microenvironment or intrinsic properties of a subpopulation of HSCs affected by clonal hematopoiesis (CH). To address this, the authors can perform genotyping of transcriptomes (GoT) on old healthy donors with CH. By comparing the transcriptomes of cells with and without CH mutations, we can evaluate the effects of CH on age-associated molecular alterations.

We thank the reviewer for the comment. Unfortunately, in order to perform GoT (genotyping of transcriptomes) on the healthy donors, requires modifying the standard 10x Genomics workflow to amplify the targeted locus and transcript of interest. This would require collecting new samples, optimizing the method and performing new analysis from scratch (from sequencing up to analysis). We believe this is not in the scope of the manuscript. On the other hand, we don’t have enough material to create new single cell libraries, this fact would require the addition of new donors and as a result, a complete new analysis to perform the integration.

Reviewer #3 (Public Review):

The authors have performed a transcriptional analysis of young/aged hematopoietic stem/progenitor cells which were obtained from normal individuals and those with MDS.

The authors generated an important and valuable dataset that will be of considerable benefit to the field. However, the data appear to be over-interpreted at times (for example, GSEA analysis does not have "functionality", as the authors claim). On the other hand, a comparison between normal-aged HSC and HSC from MDS patients appears to be under-explored in trying to understand how this disease (which is more common in the elderly) disrupts HSC function.

A more extensive cross-referencing of other normal HSPC/MDS HSCP datasets from aged humans would have been helpful to highlight the usefulness of the analytical tools that the authors have generated.

Major points

1) The authors detail methodology for identification of cell types from single-cell data - GLMnet. This portion of the text needs to be clarified as it is not immediately clear what it is or how it's being used. It also needs to be explained by what metric the classifier "performed better among progenitor cell types" and why this apparent advantage was sufficient to use it for the subsequent analysis. This is critical since interpretation of the data that follows depends on the validation of GLMnet as a reliable tool.

We thank the review for the comment. We have updated the corresponding section to better describe how GLMnet is used and that the reasoning on why we decided to use GLMnet as our cell type annotation method instead of other available tools such as Seurat, is based on the results of the benchmark described in Figure 1-figure supplement 1. We also described the main differences between our method and Seurat (See Answer to Review 1, Question # 4).

2) The finding of an increased number of erythroid progenitors and decreased number of myeloid cells in aged HPSC is surprising since aging is known to be associated with anemia and myeloid bias. Given that the initial validation of GLMnet is insufficiently described, this result raises concerns about the method. Along the same lines, the authors report that their tool detects a reduced frequency of monocyte progenitors. How does this finding correlate with the published data on aging humans? Is monocytopenia a feature of normal aging?

We thank the reviewer for this comment, as changes in the output of HSCs as a consequence of aging are of high interest. According to the literature, there is clear evidence of the loss of lymphoid progeny with age (13,14), which goes in agreement with our results. However, in the case of the myeloid compartment, the effects of aging are not as clear. Studies in mice have indeed observed that the loss of lymphoid cells is accompanied by increased myeloid output, starting at the level of GMPs (Rossi et al. 2005; Florian et al. 2012; Min et al. 2006). But studies on human individuals have not found changes in numbers of these myeloid progenitors (Kuranda et al. 2011; Pang et al. 2011). In addition, in the mentioned studies, myeloid production was measured exclusively by its white blood cells fraction. More recent studies have focused on the other myeloid compartments: megakaryocyte and erythroid cells. Results point towards the increase of platelet-biased HSC with age (Sanjuan-Pla et al. 2013; Grover et al. 2016) and a possible expansion of megakaryocytic and erythroid progenitor populations (Yamamoto et al. 2018; Poscablo et al. 2021; Rundberg Nilsson et al. 2016), which may represent a compensatory mechanism for the ineffective differentiation towards this lineage in elderly individuals. This goes in line with the accumulation of MEPs we see in our data. Finally, and in accordance with the reduced frequency of monocyte progenitors observed, it has been shown that with increasing age, there is a gradual decline in the monocyte count (15).

Regarding the concerns about our classification method raised by the reviewer, we have performed additional validations that we describe in answers to reviewer 1 comment #4 and reviewer 2 comment #1. To further confirm that the changes in cellular proportions we found are real, we applied two additional classification methods: Seurat transfer and Celltypist (16) to the elderly donors dataset. We obtained a similar expansion in MEPs, together with reduction of monocytic progenitors with the three methods (Figure 5).

Figure 5 Classification of HSPCs from elderly donors. Barplot showing proportions of every cell subpopulation per elderly donor, resulting from three classification methods: GLMnet-based classifier, Seurat transfer and Celltypist. For the three methods, cells with prediction scores < 0,5 were labeled as “not assigned”.

3) The use of terminology requires more clarity in order to better understand what kind of comparison has been performed, i.e. whether global transcriptional profiles are being compared, or those of specific subset populations. Also, the young/aged comparisons are often unclear, i.e. it's not evident whether the authors are referring to genes upregulated in aged HSC and downregulated in young HSC or vice versa. A more consistent data description would make the paper much easier to read.

We thank the reviewer for this comment. We have updated the manuscript to provide more clarity in the description of the different comparisons made in our analyses. Most changes are located in the Transcriptional profiling of human young and elderly hematopoietic progenitor systems sub-section within the Results.

4) The link between aging and MDS is not explored but could be an informative use of the data that the authors have generated. For example, anemia is a feature of both aging and MDS whereas neutropenia and thrombocytopenia only occur in MDS. Are there any specific pathways governing myeloid/platelet development that are only affected in MDS?

Thank you for raising this comment. We believe that discriminating events that take place during healthy aging from those associated to MDS will be helpful to understand this particular disease, as it is so closely related to age. This is why, when analyzing MDS, we have considered young and elderly donors as two separate sets of healthy controls, the eldery donors being the most suitable one for comparisons with MDS samples.

With regards to the comment on myeloid and platelet development, the GSEA analysis gives potentially useful information. MYC targets and oxidative phosphorylation are significantly enriched in the MEP compartment from MDS patients when compared to elderly donors, indicating that these progenitors may recover a more active profile with the disease. Hypoxia related genes, on the other hand, are more active in HSCs and MEPs from healthy elderly donors than in MDS. Hypoxia is known to be implicated in megakaryocyte and erythroid differentiation (17)

5) MDS is a very heterogeneous disorder and while the authors did specify that they were using samples from MDS with multilineage dysplasia, more clinical details (blood counts, cytogenetics, mutational status) are needed to be able to interpret the data.

We thank the reviewer for the comment. All the clinical details for each MDS patient are included in Supplementary File 5.

Author Response

Reviewer #3 (Public Review):

Dysbiosis has a substantial impact on host physiology. Using the nematode C. elegans and E.coli as a model of host-microbe interactions, Yang et al. defined a mechanism by which the host deals with gut dysbiosis to maintain fitness. They found that accumulation of E. coli in the intestine secreted indole, a tryptophan metabolite, and activated the transcription factor DAF-16. DAF-16 induced the expression of lys-7 and lys-8, which in turn limited E. coli proliferation in the gut of worms and maintained the longevity of worms. Finally, these authors demonstrated that indole-activated DAF-16 via TRPA-1 in neurons of worms.

This study revealed a new mechanism of host-microbe interaction. The concept of their work is of broad interest and the results they present are convincing. However, there are some issues that need to be addressed to support the conclusions.

Major issues

1) The authors isolated the crude extract from a high-performance liquid chromatograph (HPLC). A candidate compound was detected by activity-guided isolation and further identified as indole with mass spectrometry and NMR data. The HPLC fractionations and activity-guided isolation experiments should be described in more detail with a schematic figure to reveal how these experiments were performed and how indole was identified. Showing a chemical characterization of indole in Figure 2A is not sufficient for the evaluation of the results. Rather, a figure comparing the fraction 26th with standard indole by MS and NMR is more appealing.

We appreciate the concerns of the reviewer. Activity-guided isolation was performed as follows: The crude extract of E. coli supernatant metabolites was divided into 45 fractions according to polarity using Ultimate 3000 HPLC (Thermofisher, Waltham, MA) coupled with automated fraction collector. After freeze-drying each fraction, 1 mg of metabolites were dissolved in DMSO for DAF-16 nuclear localization assay in worms (Please see new Supplementary Table S2). The 26th fraction with DAF-16 nuclear translocation-inducing activity was then separated on silica gel column (200-300 mesh) with a continuous gradient of decreasing polarity (100%, 70%, 50%, 30%, petroleum ether/acetone) to yield four fractions (26a-d). Only the fraction of 26b could induce DAF-16 nuclear translocation. Then the fraction was further separated using a Sephadex LH-20 column to yield 32 fractions. The 26b-11th fraction with DAF-16 nuclear translocation-inducing activity contained a single compound identified by thin layer chromatography, mass spectrometry and nuclear magnetic resonance (NMR). The compound exhibited a quasimolecular ion peak at m/z 181.0782 [M+H]+ in the positive APCI-MS, and was assigned to a molecular formula of C8H7N. A comparison of these 1H NMR and 13C NMR spectra with the data reported in the literature revealed that the compound was indole (Yagudaev, 1986). The figure shows the comparison of the 26b-11 fraction with the standard indole by MS (Author response image 1).

Author response image 1.

High resolution mass spectrum of the candidate compound and indole.

2) DAF-16::GFP was mainly located in the cytoplasm of the intestine in worms expressing daf-16p::daf-16::gfp fed live E. coli OP50 on Day 1 (Figure 1A and 1B). The nuclear translocation of DAF-16 in the intestine was increased in worms fed live E. coli OP50 on Days 4 and 7, but not in age-matched WT worms fed heat-killed (HK) E. coli OP50 (Figure 1A and 1B). Since DAF-16 functions downstream of DAF-2, have the levels of DAF-2 been tested during aging on OP50 and (HK) OP50, or with and without indole supplementation?

In response to the reviewer’s suggestion, we carried out the RT-PCR experiment in 4-day-old and 7-day-old worms. It has been shown that DAF-2 initiates a kinase cascade that leads to the phosphorylation and cytoplasmic retention of DAF-16. By contrast, a reduction in the DAF-2 signaling leads to the dephosphorylation of DAF-16, allowing its nuclear translocation. In response to the reviewer’s suggestion, we tested the expression of daf-2 in 4-day-old and 7-day-old worms fed with OP50 and (HK) OP50. We found that the mRNA levels of daf-2 were significantly increased in worms on days 4 and 7 in the presence of either live or dead E. coli OP50, compared with those in worms on day 1 (Author response image 2A). In addition, supplementation with indole did not alter the mRNA levels of daf-2 in young adult worms (Author response image 2B). To conclude, the activation of DAF-16 is independent of DAF-2.

Author response image 2.

DAF-16 nuclear translocationisindependent of DAF-2.(A) The mRNA levelsof daf-2weregradually increasedin worms with age.P< 0.01;*P< 0.001; ns, not significant. (B)The mRNA levelsof daf-2were not alteredaftertreatment withindole for 24 hours.ns, not significant.

3) In lines 155-157, the author argued that the increase in the levels of indole in worms results from the intestinal accumulation of live E. coli OP50, rather than exogenous indole produced by E. coli OP50 on the NGM plates. However, the work also showed that supplementation with indole (50-200 μM) could significantly increase the indole levels in young adult worms on Day 1 (Figure 2-figure supplement 3B), which could induce nuclear translocation of DAF-16 in worms (Figure 2B). This result suggested that worms could take in indole from outside culturing environment. The concentration of indole in OP50 and (HK) OP50 could be measured.

We appreciate the concerns of the reviewer. Reviewer #2 also pointed out this problem. In this study, our data showed that the levels of indole were 30.9, 71.9, and 105.9 nmol/g dry weight in worms fed live E. coli OP50 on days 1, 4, and 7, respectively (Figure 2C). This increase in the levels of indole in worms was accompanied by an increase in CFU of live E. coli OP50 in the intestine of worms with age (Figure 2C). In addition, we determined the levels of indole in worms fed HK E. coli OP50, and found that the levels of indole were 28.2, 31.6, and 36.1 nmol/g dry weight in worms fed HK E. coli OP50 on days 1, 4, and 7, respectively (Figure 2-figure supplement 3A). It should be noted that the levels of indole in worms fed dead E. coli OP50 on day 1 were comparable of those in worms fed live E. coli OP50 on day 1 (30.9 vs 28.2 nmol/g dry weight). However, the levels of indole were not increased in worms fed HK E. coli OP50 on days 4 and 7. Furthermore, the observation that DAF-16 was retained in the cytoplasm of the intestine in worms fed live E. coli OP50 on day 1 (Figure 1A and 1B) also indicated that indole produced by E. coli OP50 on the NGM plates is not enough to induce DAF-16 nuclear translocation. By contrast, supplementation with indole (50-200 μM) significantly increased the indole levels in worms on day 1 (Figure 2-figure supplement 3B), which could induce nuclear translocation of DAF-16 in worms (Figure 2B). Thus, the increase in the levels of indole in worms with age results from intestinal accumulation of live E. coli OP50, rather than indole produced by E. coli OP50 on the NGM plates.

4) Recent work showed that the multicopy DAF-16 transgene acts differently from the single copy GFP knock in DAF-16 transgene. Which DAF-16 transgene was used in this work?

The strain we used is TJ356. Its genotype has been described as zIs356 [daf-16p::daf-16a/b::GFP+rol-6(su1006)] (Lee, Hench, & Ruvkun, 2001; Lin, Hsin, Libina, & Kenyon, 2001), from the Caenorhabditis Genetics Center (CGC).

5) In lines 190-193, the author argued that the supplementation with indole (100 M) inhibited the CFU of E. coli K-12 in WT worms, but not daf-16(mu86) mutants, on Days 4 and 7 (Figure 3H and 3I). These results suggest that endogenous indole is involved in maintaining a normal lifespan in worms. This is overstating. The data here more likely suggest that indole could inhibit the proliferation of E. coli through DAF-16.

We really appreciate this reviewer’s preciseness. In response to the reviewer’s suggestion, we had changed "...indole is involved in maintaining a normal lifespan in worms" to "...indole produced by bacteria in the gut could inhibit the proliferation of E. coli via DAF-16 in worms".

6) Sonowal (2017) reported that AHR mediates indole-promoted lifespan extension at 16 C. Yet this work argued that RNAi knockdown of ahr-1 did not affect the nuclear translocation of DAF-16 in worms fed E. coli K12 strain on Day 7 (Figure 4-figure supplement 1A) or young adult worms treated with indole (100 M) for 24 h. The difference between these two works should be discussed.

We really appreciate this reviewer’s preciseness. It has been shown that AHR-1 mediates indole-promoted lifespan extension in worms at 16 C (Sonowal et al., 2017). However, our data show that AHR-1 is not involved in activation of DAF-16 by indole-induced nuclear translocation of DAF-16 at 20 C. This means that AHR-1 and TRPA-1-lifespan extension by indole are essentially different. In our study, indole is added to NGM plates when worms reached the young adult stage. In the study by Sonowal et al., indole is supplemented at the stage of L1 larva. In addition, lifespan of C. elegans varies at different temperatures (Xiao et al., 2013). Thus, indole may promote lifespan extension via different mechanisms, which is dependent on exposure time and temperature.

7) Sonowal (2017) conducted mRNA profiling for worms growing on K12 and K12△tnaA. Is TRPA1 in their de-regulated gene list? Have other de-regulated genes been tested in this work?

We appreciate the concerns of the reviewer. We found that TRPA-1 is not included in the de-regulated gene list. Sonowal et al. focus on the gene expression profiles in worms from L1 larvae to young adults, whereas we pay attention to gene expression profiles in worms from young adults to aged worms. Thus, we did not test the de-regulated genes in their work.

8) How does indole activate TRPA1? In the absence of trpa1, what is the concentration of indole in worms? Since TRPA1 is a channel, is there any possibility that TRPA1 is involved in the transport of indole? It is really interesting and surprising that neuronal TRPA-1, but not intestinal TRPA-1, mediates the beneficial effect of indole. How does indole specifically activate TRPA-1 in neurons to preserve the longevity of worms?

We appreciate the concerns of the reviewer. TRPA1 is a nonselective cation channel permeable to Ca2+, Na+, and K+ (Zygmunt & Hogestatt, 2014). It is unlikely that TRPA1 is capable of transporting heterocyclic organic compounds, such as indole.

In response to the reviewer’s suggestion, we detected the content of indole in trpa-1(ok999) worms. We found that the levels of indole in trpa-1(ok999) worms were slightly increased in worms on days 4 and 7, compared to those in WT worms on days 4 and 7 (Author response image 3).

Recently, Ye et al. have demonstrated that indole and indole-3-carboxaldehyde (IAld) are agonists of TRPA1, which is conserved in vertebrates (Ye et al., 2021). Thus, it is mostly likely that indole acts as an agonist of TRPA-1 in C. elegans by directly binding to TRPA-1. One possibility is that activation of TRPA-1 in neurons by indole could induce a pathway that release a neurotransmitter, which in turn triggers a signaling pathway to extend lifespan of worms via activating DAF-16 in a non-cell autonomous manner. In contrast, the activation of TRPA-1 in the intestine by indole is unable to release such a neurotransmitter. Indeed, TRPA1 induces the releasing of calcitonin gene-related peptide in perivascular sensory nerves, leading to membrane hyperpolarization and arterial dilation on smooth muscle cells (Talavera et al., 2020). Moreover, the activation of TRPA1 by indole and IAld induces the secretion of the neurotransmitter serotonin in zebrafish (Ye et al., 2021).

Author response image 3.

The indole levels in trpa-1 mutants are increased on days 4 and 7, compared with those in WT worms. *P < 0.05.

9) How neuronal- and intestinal-specific knockdown of trpa-1 by RNAi was conducted? And what is the tissue-specific expression pattern of trap-1? Speculating how indole was transported to neuron cells is pretty appealing.

We appreciate the concerns of the reviewer. SID-1 is required cell-autonomously for systemic RNAi (Winston, Molodowitch, & Hunter, 2002). Thus, the sid-1 mutants are resistant to RNAi in the neuronal- and intestinal-specific RNAi strains, sid-1 was expressed under control of the neuronal-specific unc-119 and the intestinal-specific vha-6 promoters, respectively. Although it has been reported that TRPA-1 is expressed in neurons, muscles, hypodermal cells, and the intestine, Xiao et al. proved that only TRPA-1 expressed in the intestine and neurons contributes to life extension at low temperature (Xiao et al., 2013). The transporter of indole has not been identified. In Arabidopsis, ATP-binding cassette (ABC) transporter G family 37(ABCG37) has been reported to transport a range of indole derivatives (Ruzicka et al., 2010). However, all fifteen C. elegans ABC transporters share less than 30% sequence identity with ABCG37. Thus, it is impossible to determine which one is the transport channel for indole and indole derivatives in C. elegans.

10) Supplementation with indole only up-regulated the expression of lys-7 and lys-8 in worms subjected to intestinal-specific (Figure 7-figure supplement 2C), but not neuronal-specific, RNAi of trpa-1 (Figure 7-figure supplement 2D). If this is the case, should the addition of indole specifically induce the expression of lys-7p::gfp or lys-8p::gfp in neurons?

We really appreciate this reviewer’s preciseness. Indeed, lys-7 and lys-8 are expressed in both neurons and the intestine (Author response image 4A and 7B). However, the expression of lys-8p::gfp and lys-7p::gfp in neurons was not altered in worms after treatment with indole or knockdown of trpa-1 by RNAi (Author response image 4C and 4D).

Author response image 4.

The expression of LYS-7 and LYS-8 in neurons is not altered after treatment with indole or knockdown of trpa-1 by RNAi. (A and C) Representative images of lys-7p::gfp (A) and lys-8p::gfp (C). Both lys-7 and lys-8 could be expressed in neurons and the intestine. (B and D) Quantification of fluorescent intensity of lys-7p::gfp (B) and lys-8p::gfp (D) in neurons. These results are means ± SD of three independent experiments. ns, not significant.

11) The authors demonstrated that K-12△tnaA strain had undetectable tnaA mRNA or indole levels. Furthermore, the deletion of tnaA significantly inhibited the nuclear translocation of DAF-16 in worms. However, mutations in E. coli still have non-specific effects as there are several transposon insertions or polar mutations influencing downstream genes. The authors should demonstrate that only disruption of TnaA causes the failure of nuclear translocation of DAF-16.

In response to the reviewer’s suggestion, we rescued the expression of tnaA in the K-12 △tnaA strain. As expected, the indole level of from the supernatant in the K12 △tnaA::tnaA strain cultures was 34.1 μmol/L, which was comparable of that in the K12 strain cultures (42.5 μmol/L)（new Figure 2-figure supplement 4D). In addition, DAF-16 nuclear accumulation was increased in worms grown in the K12 △tnaA::tnaA strain on days 4 and 7 (new Figure 2-figure supplement 4E).

Author Response

Reviewer #1 (Public Review):

“A sample size of 3 idiopathic seems underpowered relative to the many types of genetic changes that can occur in ASD. Since the authors carried out WGS, it would be useful to know what potential causative variants were found in these 3 individuals and even if not overlapping if they might expect to be in a similar biological pathway.

If the authors randomly selected 3 more idiopathic cell lines from individuals with autism, would these cell lines also have altered mTOR signaling? And could a line have the same cell biology defects without a change in mTOR signaling? The authors argue that the sample size could be the reason for lack of overlap of the proteomic changes (unlike the phosphor-proteomic overlaps), which makes the overlapping cell biology findings even more remarkable. Or is the phenotyping simply too crude to know if the phenotypes truly are the same?”

We appreciate these thoughtful comments and also agree that of several models, our studies indicate the possibility of mTOR alteration in multiple forms of ASD. As above, we are currently pursuing this hypothesis with newly acquired DOD support. With regard to the I-ASD population, we agree that there are a large variety of genetic changes that can occur in genetically undefined ASDs. Indeed, this is precisely why we expected to see “personalized” phenotypes in each I-ASD individual when we embarked on this study. At that time, several years ago, we had planned to expand the analyses to more I-ASD individuals to assess for additional personalized phenotypes. However, as our studies progressed, we were surprised to find convergence in our I-ASD population in terms of neurite outgrowth and migration and later proteomic results showing convergence in mTOR. We found it particularly remarkable that despite a sample size of 3 that this convergence was noted. When we had the opportunity to extend our studies to the 16p11.2 deletion population, we were thrilled to conduct the first comparison between I-ASD and a genetically defined ASD and, as such, the scope of the paper turned towards this comparison. We do agree that analyses of the other I-ASD individuals would be a beneficial endeavor, both to understand how pervasive NPC migration and neurite deficits are in autism and to assess the presence of mTOR dysregulation. Furthermore, it would be important to see whether alterations in other pathways could also lead to similar cell biological deficits, though we know that other studies of neurodevelopmental disorders have found such cellular dysregulations without reporting concurrent mTOR dysregulation. Given our current grant funding to extend these analyses, such experiments within this manuscript would not be feasible.

Regarding the phenotyping methods used, we decided to assess neurite outgrowth and migration as they are both cytoskeleton dependent processes that are critical for neurodevelopment and are often regulated by the same genes. Furthermore, similar analyses have been applied to Fragile-X Syndrome, 22q11.2 deletion syndrome, and schizophrenia NPCs (Shcheglovitov A. et al., 2013; Mor-Shaked H. et al., 2016; Urbach A. et al., 2010; Kelley D. J. et al., 2008; Doers M. E. et al., 2014; Brennand K. et al., 2015; Lee I. S. et al., 2015; Marchetto M. C. et al., 2011). As such, it seems that multiple underlying etiologies can lead to similar dysregulated cellular phenotypes that can contribute to a variety of neurodevelopmental disorders. On a more global level, there are only a few different cellular functions a developing neuron can undergo, and these include processes such as proliferation, survival, migration, and differentiation. Thus, to understand neurodevelopmental disorders, it is important to study the more “crude” or “global” cellular functions occurring during neurodevelopment to determine whether they are disrupted in disorders such as ASD. In our studies we find that there are indeed dysregulations in many of these basic developmental processes, indicating that the typical steps that occur for normal brain cytoarchitecture may be disrupted in ASD. To understand why, we then further utilized molecular studies to “zoom” in on potential mechanisms which implicated common dysregulation in mTOR signaling as one driver for these common cellular phenotypes. As suggested, we did complete WGS on all the I-ASD individuals and did not see any overlapping genetic variants between the three I-ASD individuals as mentioned in our manuscript. The genetic data was published in a larger manuscript incorporating the data (Zhou A. et al., 2023). However, there were variants that were unique to each I-ASD individual which were not seen in their unaffected family members, and it is possible these variants could be contributing to the I-ASD phenotypes. We also utilized IPA to conduct pathway analysis on the WGS data utilizing the same approach we did in analysis of p- proteome and proteome data. From WGS data, we selected high read-quality variants that were found only in I-ASD individuals and had a functional impact on protein (ie excluding synonymous variants). The enriched pathways obtained from this data were strikingly different from the pathways we found in the p-proteome analysis and are now included in supplemental Figure 6 in the manuscript. Briefly, the top 5 enriched pathways were: O-linked glycosylation, MHC class 1 signaling, Interleukin signaling, Antigen presentation, and regulation of transcription.

Reviewer #2 (Public Review):

1) I found that interpreting how differential EF sensitivity is connected to the rest of the story difficult at times. First, it is unclear why these extracellular factors were picked. These are seemingly different in nature (a neuropeptide, a growth factor and a neuromodulator) targeting largely different pathways. This limits the interpretation of the ASD subtype-specific rescue results. One way of reframing that could help is that these are pro-migratory factors instead of EFs broadly defined that fail to promote migration in I-ASD lines due to a shared malfunctioning of the intracellular migration machinery or cell-cell interactions (possibly through tight junction signaling, Fig S2A). Yet, this doesn't explain the migration/neurite phenotypes in 16p11 lines where EF sensitivity is not altered, overall implying that divergent EF sensitivity independent of underlying mTOR state. What is the proposed model that connects all three findings (divergent EF sensitivity based on ASD subtypes, 2 mTOR classes, convergent cellular phenotypes)?

We thank you for the kind assessment of our manuscript and for the thought-provoking questions posed. In terms of extracellular factors, for our study, we defined extracellular factor as any growth factor, amino acid, neurotransmitter, or neuropeptide found in the extracellular environment of the developing cells. The EFs utilized were selected due to their well-established role in regulation of early neurodevelopmental phenotypes, their expression during the “critical window” of mid-fetal development (as determined by Allan Brain Atlas), and in the case of 5-HT, its association with ASD (Abdulamir H. A. et al., 2018; Adamsen D. et al., 2014; Bonnin A. et al., 2011; Bonnin A. et al., 2007; Chen X. et al., 2015; El Marroun H. et al., 2014; Hammock E. et al., 2012; Yang C. J. et al., 2014; Dicicco-Bloom E. et al., 1998; Lu N. et al., 1998; Suh J. et al., 2001; Watanabe J. et al., 2016; Gilmore J. H. et al., 2003; Maisonpierre P. C. et al., 1990; Dincel N. et al., 2013; Levi- Montalcini R., 1987). Lastly, prior experiments in our lab with a mouse model of neurodevelopmental disorders, had shown atypical responses to EFs (IGF-1, FGF, PACAP). As such, when we first chose to use EFs in human NPCs we wanted to know 1) whether human NPCs even responded to these EFs, 2) whether EFs regulated neurite outgrowth and migration and 3) would there be a differential response in NPCs derived from those with ASD. Our studies were initiated on the I-ASD cohort and given the heterogeneity of ASD we had hypothesized we would get “personalized” neurite and migration phenotypes. Due to this reason, we also wanted to select multiple types of EFs that worked on different signaling pathways. Ultimately, instead of personalized phenotypes we found that all the I-ASD NPCs did not respond to any of the EFs tested whereas the 16p11.2 deletion NPCS did – this was therefore the only difference we found between these two “forms” of ASD. As noted, in I-ASD the lack of response to EFs can be ameliorated by modulating mTOR. However, in the 16p11.2 deletion, despite similar mTOR dysregulation as seen in I-ASD, there is no EF impairment. We do not have a cohesive model to explain why the 16pDel individuals differ from the I-ASD model other than to point to the p- proteomes which do show that the 16pDel NPCs are distinct from the I-ASD NPCs. It seems that mTOR alteration can contribute to impaired EF responsiveness in some NPCs but perhaps there is an additional defect that needs to be present in order for this defect to manifest, or that 16p11.2 deletion NPCs have specific compensatory features. For example, as noted in the thoughtful comment, the p-proteome canonical pathway analysis shows tight junction malfunction in I-ASD which is not present in the 16pDel NPCs and it could be the combination of mTOR dysregulation + dysregulated tight junction signaling that has led to lack of response to EFs in I-ASD. Regardless, we do not think the differences between two genetically distinct ASDs diminish the convergent mTOR results we have uncovered. That is, regardless of whatever defects are present in the ASD NPCs, we are able to rescue it with mTOR modulation which has fascinating implications for treatment and conceptualization for ASD. Lastly, we see our EF studies as an important inclusion as it shows that in some subtypes of ASD, lack of response to appropriate EFs could be contributing to neurodevelopmental abnormalities. Moreover, lack of response to these EFs could have implications for treatment of individuals with ASD (for example, SSRI are commonly used to treat co-morbid conditions in ASD but if an individual is unresponsive to 5- HT, perhaps this treatment is less effective). We have edited the manuscript to include an additional discussion section to address the EFs more thoroughly and have included a few extra sentences in the introduction as well!

2) A similar bidirectional migration phenotype has been described in hiSPC-derived human cortical interneurons generated from individuals with Timothy Syndrome (Birey et al 2022, Cell Stem Cell). Here, authors show that the intracellular calcium influx that is excessive in Timothy Syndrome or pharmacologically dampened in controls results in similar migration phenotypes. Authors can consider referring to this report in support of the idea that bimodal perturbations of cardinal signaling pathways can converge upon common cellular migration deficits.

We thank you for pointing out the similar migration phenotype in the Timothy Syndrome paper and have now cited it in our manuscript. We have also expanded on the concept of “too much or too little” of a particular signaling mechanism leading to common outcomes.

3) Given that authors have access to 8 I-ASD hiPSC lines, it'd very informative to assay the mTOR state (e.g. pS6 westerns) in NPCs derived from all 8 lines instead of the 3 presented, even without assessing any additional cellular phenotypes, which authors have shown to be robust and consistent. This can help the readers better get a sense of the proportion of high mTOR vs low- mTOR classes in a larger cohort.

We have already addressed this in response to reviewer 1 and the essential revisions section, providing our reasoning for not expanding the study to all 8 I-ASD individuals.

4) Does the mTOR modulation rescue EF-specific responses to migration as well (Figure 7)

We did not conduct sufficient replicates of the rescue EF specific responses to migration due to the time consuming and resource intensive nature of the neurosphere experiments. Unlike the neurite experiments, the neurosphere experiments require significantly more cells, more time, selection of neurospheres based on a size criterion, and then manual trace measurements. We did one experiment in Family-1 where we utilized MK-2206 to abolish the response of Sib NPCs to PACAP. Likewise, adding SC-79 to I-ASD-1 neurospheres allowed for response to PACAP.

Author response image 1.

Author response image 2.

Reviewer #3: Public Review

We appreciate the kind, detailed and very thorough review you provided for us!

The results on the mTOR signaling pathway as a point of convergence in these particular ASD subtypes is interesting, but the discussion should address that this has been demonstrated for other autism syndromes, and in the present manuscript, there should be some recognition that other signaling pathways are also implicated as common factors between the ASD subtypes.

With regards to the mTOR pathway, we had included the other ASD syndromes in which mTOR dysregulation has been seen including tuberous sclerosis, Cowden Syndrome, NF-1, as well as Fragile-X, Angelman, Rett and Phelan McDermid in the final paragraph of the discussion section “mTOR Signaling as a Point of Convergence in ASD”. We have now expanded our discussion to include that other signaling pathways such as MAPK, cyclins, WNT, and reelin which have also been implicated as common factors between the ASD subtypes.

The conclusions of this paper are mostly well supported by data, but for the cell migration assay, it is not clear if the authors control for initial differences in the inner cell mass area of the neurospheres in control vs ASD samples, which would affect the measurement of migration.

Thank you for this thoughtful comment! When we first started our migration data, inner cell mass size was indeed a major concern for which we controlled in our methods. First, when plating the neurospheres, we would only collect spheres when a majority of spheres were approximately a diameter of 100 um. Very large spheres often could not be imaged due to being out of focus and very small spheres would often disperse when plated. Thus, there were some constraints to the variability of inner cell mass size.

Furthermore, when we initially collected data, we conducted a proof of principal test to see if initial inner cell mass area (henceforth referred to as initial sphere size or ISS) influenced migration data. To do so, we obtained migration and ISS data from each diagnosis (Sib, NIH, I-ASD, 16pASD). Then we utilized R studio to see if there is a relationship between Migration and ISS in each diagnosis category using the equation (lm(Migration~ISS, data=bydiagnosis). In this equation, lm indicates linear modeling and (~) is a term used to ascertain the relationship between Migration and ISS and the term data=bydiagnosis allows the data to be organized by diagnosis

The results were expressed as R-squared values indicating the correlation between ISS and Migration for each diagnosis and the p-value showing statistical significance for each comparison. As shown in Author response table 1, for each data set, there is minimal correlation between Migration and ISS in each data set. Moreover, there are no statistically significant relationships between Migration and ISS indicating that initial sphere size DOES NOT influence migration data in any of our data-sets.

Author response table 1.

Lastly, utilizing R, we modeled what predicted migration would be like for Sib, NIH, I-ASD, and 16pASD if we accounted for ISS in each group. Raw migration data was then plotted against the predicted data as in Author response image 3.

Author response image 3.

As shown in the graph, there are no statistical differences between the raw migration data (the data that we actually measured in the dish) and the modeled data in which ISS is accounted for as a variable. As such, we chose not to normalize to or account for ISS in our other experiments. We have now included the above R studio analyses in our supplemental figures (Figure S1) as well.

Also, in Fig 5 and 6, panels I and J omit the effects of drug on mTOR phosphorylation as shown for other conditions.

Both SC-79 and MK2206 were selected in our experiments after thorough analysis of their effects on human epithelial cells and other cultured cells (citations in manuscript). However, initially, we did not know whether either of these drugs would modulate the mTOR pathway in human NPCs, thus, in Figures 5A,5D, 6A and 6D we chose to focus on two of our data-sets to establish the effect of these drugs in human NPCs. Our experiments in Family-1 and Family-2 showed us that SC-79 increases PS6 in human NPCs while MK-2206 downregulates it. Once this was established, we knew the drugs would have similar effects in the NPCs from the other families. Thus, we only conducted a proof of principle test to confirm the drug does indeed have the intended effect in I-ASD-3 and 16pDel. We have included these proof of principle westerns in Figure 5I, 5K, 6I and 6K to show that the effects of these drugs are reproducible across all our NPC lines. We did not include quantification since the data is only from our single proof of principle western.

Author Response

Reviewer #1 (Public Review):

Using fMRI-based univariate and multivariate analyses, Root, Muret, et al. investigated the topography of face representation in the somatosensory cortex of typically developed two-handed individuals and individuals with a congenital and acquired missing hand. They provide clear evidence for an upright face topography in the somatosensory cortex in all three groups. Moreover, they find that one-handers, but not amputees, show shorter distances from lip representations to the hand area, suggesting a remapping of the lips. They also find a shift away of the upper face from the deprived hand area in one-handers, and significantly greater dissimilarity between face part representations in amputees and one-handers. The authors argue that this pattern of remapping is different to that of cortical neighborhood theories and points toward a remapping of face parts which have the ability to compensate for hand function, e.g., using the lips/mouth to manipulate an object.

These findings provide interesting insights into the topographic organization of face parts and the principles of cortical (re)organization. The authors use several analytical approaches, including distance measures between hand- and face-part-responsive regions and representational similarity analysis (RSA). Particularly commendable is the rigorous statistical analysis, such as the use of Bayesian comparisons, and careful interpretation of absent group differences.

We thank the reviewer for their positive and constructive feedback.

Reviewer #2 (Public Review):

After amputation, the deafferented limb representation in the somatosensory cortex is activated by stimulation of other body parts. A common belief is that the lower face, including the lips, preferentially "invades" deafferented cortex due to its proximity to cortex. In the present study, this hypothesis is tested by mapping the somatosensory cortex using fMRI as amputees, congenital one-handers, and controls moved their forehead, nose, lips or tongue. First, they found that, unlike its counterpart in monkeys, the representation of the face in the somatosensory cortex is right-side up, with the forehead most medial (and abutting the hand) and the lips most lateral. Second, there was little evidence of "reorganization" of the deafferented cortex in amputees, even when tested with movements across the entire face rather than only the lips. Third, congenital one-handers showed significant reorganization of deafferented cortex, characterized principally by the invasion of the lower face, in contrast to predictions from the hypothesis that proximity was the driving factor. Fourth, there was no relationship between phantom limb pain reports and reorganization.

As a non-expert in fMRI, I cannot evaluate the methodology. That being said, I am not convinced that the current consensus is that the representation of the face in humans is flipped compared to that of monkeys. Indeed, the overwhelming majority of somatosensory homunculi I have seen for humans has the face right side up. My sense is that the fMRI studies that found an inverted (monkey-like) face representation contradict the consensus.

Thank you for point this out. As we tried to emphasise in the introduction, very few neuroimaging studies actually investigated face somatotopy in humans, with inconsistent results. We agree the default consensus tends to be dominated by the up-right depiction of Penfield’s homunculus (recently replicated by Roux et al, 2018). However, due to methodological and practical constraints, alignment across subjects in the case of intracortical recordings is usually difficult to achieve, and thus makes it difficult to assess the consistency in topographical organisation. Moreover, previous imaging studies did not manage to convincingly support Penfield’s homunculus. For these two key reasons, the spatial orientation of the human facial homunculus is still debated. A further limiting factor of previous studies in humans is that the vast majority of human studies investigating face (re)mapping in humans focused solely on the lip representation, using the cortical proximity hypothesis to interpret their results. Consequently, as we highlight above in our response to the Editor, there is a wide-spread and false representation in the human literature of the lips neighbouring the hand area.

To account for the reviewer’s critic and convey some of this context, we changed our title from: Reassessing face topography in primary somatosensory cortex and remapping following hand loss; to: Complex pattern of facial remapping in somatosensory cortex following congenital but not acquired hand loss. This was done to de-emphasise the novelty of face topography relative to our other findings.

We also rewrote our introduction (lines 79-94) as follows:

“The research focus on lip cortical remapping in amputees is based on the assumption that the lips neighbour the hand representation. However, this assumption goes against the classical upright orientation of the face in S126–30, as first depicted in Penfield’s Homunculus and in later intracortical recordings and stimulation studies26–29, with the upper-face (i.e., forehead) bordering the hand area. In contrast, neuroimaging studies in humans studying face topography provided contradictory evidence for the past 30 years. While a few neuroimaging studies provided partial evidence in support of the traditional upright face organisation31, other studies supported the inverted (or ‘upside-down’) somatotopic organisation of the face, similar to that of non-human primates32,33. Other studies suggested a segmental organisation34, or even a lack of somatotopic organisation35–37, whereas some studies provided inconclusive or incomplete results38–41. Together, the available evidence does not successfully converge on face topography in humans. In line with the upright organisation originally suggested by Penfield, recent work reported that the shift in the lip representation towards the missing hand in amputees was minimal42,43, and likely to reside within the face area itself. Surprisingly, there is currently no research that considers the representation of other facial parts, in particular the upper-face (e.g., the forehead), in relation to plasticity or PLP.”

We also updated the discussion accordingly (lines 457, 469-477, 490-492).

Similarly, it is not clear to me how the observations (1) of limited reorganization in amputees, (2) of significant reorganization in congenital one-handers, and (3) of the lack of relationship between PLP and reorganization is novel given the previous work by this group. Perhaps the authors could more clearly articulate the novelty of these results compared to their previous findings.

Thank you for giving us the opportunity to clarify on this important point. The novelty of these results can be summarised as follow:

(1) Conceptually, it is crucial for us to understand if deprivation-triggered plasticity is constrained by the local neighbourhood, because this can give us clues regarding the mechanisms driving the remapping. We provide strong topographic evidence about the face orientation in controls, amputees and one-handers.

(2) The vast majority of previous research on brain plasticity following hand loss (both congenital and acquired) in humans has exclusively focused on the lower face, and lips in particular. We provide systematic evidence for stable organisation and remapping of the neighbouring upper face, as well as the lower face. We also study topographic representation of the tongue (and nose) for the first time.

(3) The vast majority of previous research on brain remapping following hand loss (both congenital and acquired, neuroimaging and electrophysiological) was focused on univariate activity measures, such as the spatial spread of units showing a similar feature preference, or the average activity level across individual units. We are going beyond remapping by using RSA, which allows us to ask not only if new information is available in the deprived cortex (as well as the native face area), but also whether this new information is structured consistently across individuals and groups. We show that representational content is enhanced in the deprived cortex one-handers whereas it is stable in amputees relative to controls (and to their intact hand region).

(4) Based on previous studies, the assumption was that reorganisation in congenital one-handers was relatively unspecific, affecting all tested body parts. Here, we provide evidence for a more complex pattern of remapping, with the forehead representation seemingly moving out of the missing hand region (and the nose representation being tentatively similar to controls). That is, we show not just “invasion” but also a shift of the neighbour away from the hand area which has never been documented (or in fact suggested).

(5) Using Bayesian analyses we provide definitive evidence against a relationship between PLP and forehead remapping, providing first and conclusive evidence against the remapping hypothesis, based on cortical neighbourhood.

Our inclination is not to add a summary paragraph of these points in our discussion, as it feels too promotional. Instead, we have re-written large sections of the introduction and discussion to better emphasise each of these points separately throughout the text, where the context is most appropriate. Given the public review strategy taken by eLife, the novelty summary provided above will be available for any interested reader, as part of the public review process. However, should the reviewer feel that a novelty summary paragraph is required (or an emphasis on any of the points summarised above), we will be happy to revise the manuscript accordingly.

Finally, Jon Kaas and colleagues (notably Niraj Jain) have provided evidence in experiments with monkeys that much of the observed reorganization in the somatosensory cortex is inherited from plasticity in the brain stem. Jain did not find an increased propensity for axons to cross the septum between face and hand representations after (simulated) amputation. From this perspective, the relevant proximity would be that of the cuneate and trigeminal nuclei and it would be critical to map out the somatotopic organization of the trigeminal and cuneate nuclei to test hypotheses about the role of proximity in this remapping.

Thank you for highlighting this very relevant point, which we are well aware of. We fully agree with the reviewer that this is an important goal for future study, but functional imaging of the brainstem in humans is particularly challenging and would require ultra high field imaging (7T) and specialised equipment. We have encountered much local resistance due to hypothetical issues for MRI safety for scanning amputees in this higher field strength, meaning we are unable to carry out this research ourselves. Our former lab member Sanne Kikkert, who is now running her independent research programme in Zurich, has been working towards this goal for the past 4 years. So we can say with confidence that this aim is well beyond the scope of the current study. In response to your comment, we mentioned this potential mechanism in the introduction (lines 98-101), we ensured that we only referred to “cortical proximity” throughout our manuscript, and we circle back to this important point in the discussion.

Lines 539-543: “Moreover, even if the remapping we observed here goes against the theory of cortical proximity, it can still arise from representational proximity at the subcortical level, in particular at the brainstem level44,45. While challenging in humans, mapping both the cuneate and trigeminal nuclei would be critical to provide a more complete picture regarding the role of proximity in remapping.”

Reviewer #3 (Public Review):

In their study, the authors set up to challenge the long-held claim that cortical remapping in the somatosensory cortex in hand deprived cortical territories follows somatotopic proximity (the hand region gets invaded by cortical neighbors) as classically assumed. In contrast to this claim, the authors suggest that remapping may not follow cortical proximity but instead functional rules as to how the effector is used. Their data indeed suggest that the deprived hand area is not invaded by the forefront which is the cortical neighbor but instead by the lips which may compensate for hand loss in manipulating objects. Interestingly the authors suggest this is mostly the case for one-handers but not in amputees for who the reorganization seems more limited in general (but see my comments below on this last point).

This is a remarkably ambitious study that has been skilfully executed on a strong number of participants in each group. The complementarity of state-of-the-art uni- and multi-variate analyses are in the service of the research question, and the paper is clearly written. The main contribution of this paper, relative to previous studies including those of the same group, resides in the mapping of multiple face parts all at once in the three groups.

We are grateful to the reviewer for appreciating the immense effort that this study involved.

In the winner takes all approach, the authors only include 3 face parts but exclude from the analyses the nose and the thumb. I am not fully convinced by the rationale for not including nose in univariate analyses - because it does not trigger reliable activity - while keeping it for representational similarity analyses. I think it would be better to include the nose in all analyses or demonstrate this condition is indeed "noisy" and then remove it from all the analyses. Indeed, if the activity triggered by nose movement is unreliable, it should also affect multivariate.

Following this comment, we re-ran all univariate analyses to include the nose, and updated throughout the main text and supplemental results and related figures. In short, adding the nose did not change the univariate results, apart from a now significant group x hemisphere interaction for the CoG of the tongue when comparing amputees and controls, matching better the trends for greater surface coverage in the deprived hand ROI of amputees. Full details are provided in our response to Reviewer 1 above.

The rationale for not including the hand is maybe more convincing as it seems to induce activity in both controls and amputees but not in one-handers. First, it would be great to visualize this effect, at least as supplemental material to support the decision. Then, this brings the interesting possibility that enhanced invasion of hand territory by lips in one-handers might link to the possibility to observe hand-related activity in the presupposed hand region in this population. Maybe the authors may consider linking these.

Thank you for this comment. As we explain in our response to Reviewer 1 above, we did not intent the thumb condition in one-handers for analysis, as the task given to one-handers (imagine moving a body part you never had before) is inherently different to that given to the other groups (move - or at least attempt to move - your (phantom) hand). As such, we could not pursuit the analysis suggested by the reviewer here. To reduce the discrepancy and following Reviewer 1’s advice, we decided to remove the hand-face dissimilarity analysis which we included in our original manuscript, and might have sparked some of this interest. Upon reflection we agreed that this specific analysis does not directly relate to the question of remapping (but rather of shared representation), in addition to making the paper unbalanced. We will now feature this analysis in another paper that appears more appropriate in the context of referred sensations in amputees (Amoruso et al, 2022 MedRxiv).

The use of the geodesic distance between the center of gravity in the Winner Take All (WTA) maps between each movement and a predefined cortical anchor is clever. More details about how the Center Of Gravity (COG) was computed on spatially disparate regions might deserve more explanations, however.

We are happy to provide more detail on this analysis, which weights the CoG based on the clusters size (using the workbench command -metric-weighted-stats). Let’s consider the example shown here (Figure 1) for a single control participant, where each CoG is measured either without weighting (yellow vertices) or with cluster weighting (forehead CoG=red, lip CoG=dark blue, tongue CoG=dark red). When the movement produces a single cluster of activity (the lips in the non-dominant hemisphere, shown in blue), the CoG’s location was identical for both weighted (red) and unweighted (yellow) calculations. But other movements, such as the tongue (green), produced one large cluster (at the lateral end), with a few more disparate smaller clusters more medially. In this case, the larger cluster of maximal activity is weighted to a greater extent than the smaller clusters in the CoG calculation, meaning the CoG is slightly skewed towards it (dark red), relative to the smaller clusters.

Figure 1. Centre-of-gravity calculation, weighted and unweighted by cluster size, in an example control participant. Here the winner-takes-all output for each facial movement (forehead=red, lips=blue, tongue=green) was used to calculate the centre-of-gravity (CoG) at the individual-level in both the dominant (left-hand side) and non-dominant (right-hand side) hemisphere, weighted by cluster size (forehead CoG=red, lip CoG=dark blue, tongue CoG=dark red), compared to an unweighted calculation (denoted by yellow dots within each movements’ winner-takes-all output).

This is now explained in the methods (lines 760-765) as follows:

“To assess possible shifts in facial representations towards the hand area, the centre-of-gravity (CoG) of each face-winner map was calculated in each hemisphere. The CoG was weighted by cluster size meaning that in the event of multiple clusters contributing to the calculation of a single CoG for a face-winner map, the voxels in the larger cluster are overweighted relative to those in the smaller clusters. The geodesic cortical distance between each movement’s CoG and a predefined cortical anchor was computed.”

Moreover, imagine that for some reason the forefront region extends both dorsally and ventrally in a specific population (eg amputees), the COG would stay unaffected but the overlap between hand and forefront would increase. The analyses on the surface area within hand ROI for lips and forehead nicely complement the WTA analyses and suggest higher overlap for lips and lower overlap for forehead but none of the maps or graphs presented clearly show those results - maybe the authors could consider adding a figure clearly highlighting that there is indeed more lip activity IN the hand region.

We agree with you on this limitation of the CoG and this is why we interpret all cortical distances analyses in tandem with the laterality indices. The laterality indices correspond to the proportion of surface area in the hand region for a given face part in the winner-maps.

Nevertheless, to further convince the Reviewer, we extracted activity levels (beta values) within the hand region of congenitals and controls, and we ran (as for CoGs) a mixed ANOVA with the factors Hemisphere (deprived x intact) and Group (controls x one-handers).

As expected from the laterality indices obtained for the Lips, we found a significant group x hemisphere interaction (F(1,41)=4.52, p=0.040, n2p=0.099), arising from enhanced activity in the deprived hand region in one-handers compared to the non-dominant hand region in controls (t(41)=-2.674, p=0.011) and to the intact hand region in one-handers (t(41)=-3.028, p=0.004).

Since this kind of analysis was the focus of previous studies (from which we are trying to get away) and since it is redundant with the proportion of face-winner surface coverage in the hand region, we decided not to include it in the paper. But we could add it as a Supplementary result if the Reviewer believes this strengthens our interpretation.

In addition to overlap analyses between hand and other body parts, the authors may also want to consider doing some Jaccard similarity analyses between the maps of the 3 groups to support the idea that amputees are more alike controls than one-handers in their topographic activity, which again does not appear clear from the figures.

We thank the reviewers for this clever suggestion. We now include the Jaccard similarity analysis, which quantified the degree of similarity (0=no overlap between maps; 1=fully overlapping) between winner-takes-all maps (which included the nose; akin to the revised univariate results) across groups. For each face part/amputee, the similarity with the 22 controls and 21 one-handers respectively was averaged. We utilised a linear mixed model which included fixed factors of Group (One-handers x Controls), Movement (Forehead x Nose x Lips x Tongue) and Hemisphere (Intact x Deprived) on Jaccard similarity values (similar to what we used for the RSA analysis). A random effect of participant, as well as covariates of ages, were also included in the model.

Results showed a significant group x hemisphere interaction (F(240.0)=7.70, p=0.006; controlled for age; Fig. 5), indicating that amputees’ maps showed different similarity values to controls’ and one-handers’ depending on the hemisphere. Post-hoc comparisons (corrected alpha=0.025; uncorrected p-values reported) revealed significantly higher similarity to controls’ than to one-handers’ maps in the deprived hemisphere (t(240)=-3.892, p<.001). Amputees’ maps also showed higher similarity to controls’ maps in the deprived relative to the intact hemisphere (t(240)=2.991, p=0.003). Amputees, therefore, displayed greater similarity of facial somatotopy in the deprived hemisphere to controls, suggesting again fewer evidence for cortical remapping in amputees.

We added these results at the end of the univariate analyses (lines 335-351) and in the discussion (lines 464-465 and 497-500).

This brings to another concern I have related to the claim that the change in the cortical organization they observe is mostly observed in one-handers. It seems that most of this conclusion relies on the fact that some effects are observed in one-handers but not in amputees when compared to controls, however, no direct comparisons are done between amputees and one-handers so we may be in an erroneous inference about the interaction when this is actually not tested (Nieuwenhuis, 11). For instance, the shift away from the hand/face border of the forehead is also (mildly) significant in amputees (as observed more strongly in one-handers) so the conclusion (eg from the subtitle of the results section) that it is specific to one-hander might not fully be supported by the data. Similar to the invasion of the hand territory from the lips which is significant in amputees in terms of surface area. All together this calls for toning down the idea that plasticity is restricted to congenital deprivation (eg last sentence of the abstract). Even if numerically stronger, if I am not wrong, there are no stats showing remapping is indeed stronger in one-handers than in amputees and actually, amputees show significant effects when compared to controls along the lines as those shown (even if more strongly) in one-handers.

Thank you for this very important comment. We fully agree – the RSA across-groups comparison is highly informative but insufficient to support our claims. We did not compare the groups directly to avoid multiple comparisons (both for statistical reasons and to manage the size of the results section). But the reviewer’s suggestion to perform a Jaccard similarity analysis complements very nicely the univariate and multivariate results and allows for a direct (and statistically lean) comparison between groups, to assess whether amputees are more similar to controls or to congenital one-handers, taking into account all aspects of their maps (both spatial location/CoG and surface coverage). We added the Jaccard analysis to the main text, at the end of the univariate results (lines 335-385). The Jaccard analysis suggests that amputees’ maps in the deprived hemisphere were more similar to the maps of controls than to the ones of congenital one-handers. This allowed us to obtain significant statistical results to support the claim that remapping is indeed stronger in one-handers than in amputees (lines 346-351). We also compared both amputees and one-handers to the control group. In line with our univariate results, this revealed that the only face part for which controls were more similar to one-handers than to amputees was the tongue (lines 379-381). And that the forehead remapping observed at the univariate level in amputees (surface area), is likely to arise from differences in the intact hemisphere (lines 381-383).

Finally, we also added the post-hoc statistics comparing amputees to congenitals in the RSA analysis (lines 425-427): “While facial information in the deprived hand area was increased in one-handers compared with amputees, this effect did not survive our correction for multiple comparisons (t(70.7)=-2.117, p=0.038).”

Regarding the univariate results mentioned by the reviewer, we would like to emphasise that we had no significant effect for the lips in amputees, though we agree the surface area appears in between controls and one-handers. But this laterality index was not different from zero. This test is now added lines 189-190. Regarding the forehead, we fully agree with the Reviewer, and we adjusted the subtitle accordingly (lines 241-242). For consistency, we also added the t-test vs zero for the forehead surface area (non-significant, lines 251-253).

Also, maybe the authors could explore whether there is actually a link between the number of years without hand and the remapping effects.

To address this question, we explored our data using a correlation analysis. The only body part who showed some suggestive remapping effects was the tongue, and so we explored whether we could find a relationship (Pearson’s correlation) between years since amputation and the laterality index of the Tongue in amputees (r = 0.007, p=0.980, 95% CI [-0.475, 0.475]). We also explored amputees’ global Jaccard similarity values to controls in the deprived hemisphere (r = -0.010, p=0.970, 95% CI [-0.488, 0.473]), and could not find any relationship. Considering there was no strong remapping effect to explain, we find this result too exploratory to include in our manuscript.

One hypothesis generated by the data is that lips remap in the deprived hand area because lips serve compensatory functions. Actually, also in controls, lips and hands can be used to manipulate objects, in contrast to the forehead. One may thus wonder if the preferential presence of lips in the hand region is not latent even in controls as they both link in functions?

We agree with the reviewer’s reasoning, and we think that the distributed representational content we recently found in two-handers (Muret et al, 2022) provides a first hint in this direction. It is worth noting that in that previous publication we did not find differences across face parts in the activity levels obtained in the hand region, except for slightly more negative values for the tongue. But we do think that such latent information is likely to provide a “scaffolding” for remapping. While the design of our face task does not allow to assess information content for each face part (as done for the lips in Muret et al, 2022), this should be further investigated in follow-up studies.

We added a sentence in the discussion to highlight this interesting notion: Lines 556-559: “Together with the recent evidence that lip information content is already significant in the hand area of two-handed participants (Muret et al, 2022), compensatory behaviour since developmental stages might further uncover (and even potentiate) this underlying latent activity.”

Author Response

Reviewer #1 (Public Review):

The authors used data from extracellular recordings in mouse piriform cortex (PCx) by Bolding & Franks (2018), they examined the strength, timing, and coherence of gamma oscillations with respiration in awake mice. During "spontaneous" activity (i.e. without odor or light stimulation), they observed a large peak in gamma that was driven by respiration and aligned with the spiking of FBIs. TeLC, which blocks synaptic output from principal cells onto other principal cells and FBIs, abolishes gamma. Beta oscillations are evoked while gamma oscillations are induced. Odors strongly affect beta in PCx but have minimal (duration but not amplitude) effects on gamma. Unlike gamma, strong, odor-evoked beta oscillations are observed in TeLC. Using PCA, the authors found a small subset of neurons that conveyed most of the information about the odor (winner cells). Loser cells were more phase-locked to gamma, which matched the time course of inhibition. Odor decoding accuracy closely follows the time course of gamma power.

We thank the reviewer for the accurate summary of our work.

I think this is an interesting study that uses a publicly available dataset to good effect and advances the field elegantly, especially by selectively analyzing activity in identified principal neurons versus inhibitory interneurons, and by making use of defined circuit perturbations to causally test some of their hypotheses.

We thank the reviewer for the positive appraisal.

Major:

• The authors show odor-specificity at the time of the gamma peak and imply that the gamma coupling is important for odor coding. Is this because gamma oscillations are important or because gamma is strongest when activity in PCx is strongest (i.e. both excitatory and inhibitory activity, which would cancel each other in the population PSTH, which peaks earlier)? To make this claim, the authors could show that odor decoding accuracy - with a small (~10 ms sliding window) - oscillates at approx. gamma frequencies. As is, Fig. 5 just shows that cells respond at slightly different times in the sniff cycle. What time window was used for computing the Odor Specificity Index? Put another way, is it meaningful that decoding is most accurate when gamma oscillations are strongest, or is this just a reflection of total population activity, i.e., when activity is greatest there is more gamma power, and odor decoding accuracy is best?

We thank the reviewer for the critical comment. Please note that the employed decoding strategy (supervised learning with cross-validation) prevents us from quantifying a time series of decoding accuracy. Nevertheless, to overcome this difficulty, we divided the spike data (0-500 ms following the inhalation start) according to the gamma cycle into four non-overlapping gamma phase bins. Then we tested whether odor decoding accuracy varied as a function of the gamma cycle phase. Using this approach, we found that decoding depended on the gamma phase, as shown below:

(The bottom plot shows the modulation of decoding accuracy within the gamma cycle [Real MI] compared to a surrogate distribution [Surr MI, obtained by circularly shifting the gamma phases by a random amount]).

We interpret this new result as indicative that gamma influences decoding accuracy directly and that our previous result was not only a reflection of total population activity. Moreover, please note that we only use the principal cell activity for computing the odor specificity index (Fig 5E) and decoding accuracy (Fig 7B). Both peak at ~150 ms following inhalation start, at a time window where the net principal cell activity is roughly similar to baseline levels (Fig 5A bottom panel).

These new panels were added to revised Figure 7 and mentioned in the revised manuscript (page 8); we now also discuss the above considerations about maximal decoding not coinciding with the peak firing rate (page 10).

Regarding the Odor Specificity Index computation, we apologize for not describing it appropriately in the corresponding Methods subsection. We employed the same sliding time window as in the population vector correlation and the decoding analyses (i.e., 100 ms window, 62.5 % overlap). This information has been added to the revised manuscript (page 15).

• The authors say, "assembly recruitment would depend on excitatory-excitatory interactions among winner cells occurring simultaneously during gamma activity." Can the authors test this prediction by examining the TeLC recordings, in which excitatory-excitatory connections are abolished?

We thank the reviewer for the relevant comment. We followed the reviewer's suggestion and analyzed odor assemblies in TeLC recordings. Interestingly, we found a greater increase in the firing rate of winner cells in TeLC recordings (see figure below), which therefore does not support our previous interpretation that assembly recruitment would depend on excitatory-excitatory local interactions.

Thus, this new result suggests a much more critical role than we previously considered for the OB projections in determining winner neurons.

Moreover, we found significant differences in the properties of loser cells. In particular, the TeLC-infected piriform cortex showed a decreased number of losing cells, which were significantly less inhibited than their contralateral counterparts:

Furthermore, the reduced inhibition of losing cells was associated with an increased correlation of assembly weights across odors for the affected hemisphere:

Therefore, we believe these results highlight the role of gamma oscillations in segregating cell assemblies and generating a sparse orthogonal odor representation in the piriform cortex. These findings are now included as new panels of Figure 6 and discussed on page 8. Noteworthy, to conform with them, we modified our speculative sentence (page 9) "assembly recruitment would depend on excitatory-excitatory interactions among winner cells occurring simultaneously during gamma activity" to “(…) the assembly recruitment would depend on OB projections determining which winner cells “escape” gamma inhibition, highlighting the relevance of the OB-PCx interplay for olfaction (Chae et al., 2022; Otazu et al., 2015).”

• The authors show that gamma oscillations are abolished in the TeLC condition and use this to claim that gamma arises in the PCx. However, PCx neurons also project back to the OB, where they form excitatory connections onto granule cells. Fukunaga et al (2012) showed that granule cells are essential for generating gamma oscillations in the bulb. Can the authors be sure that gamma is generated in the PCx, per se, rather than generated in the bulb by centrifugal inputs from the PCx, and then inherited from the bulb by the PCx?

We thank the reviewer for the pertinent comment regarding gamma generation in the PCx. To address this point, we have performed current source density (CSD) analysis, which showed sink and sources of low-gamma oscillations within the PCx and also a phase reversal:

This result – shown as panel F in Figure 1 – suggests a local generation of gamma within the PCx. Along with the fact that PCx gamma tightly correlates with piriform FBI firing and that PCx gamma disappears in the TeLC ipsi hemisphere, which has intact OB projections, we deem it more parsimonious to assume that gamma does originate in the piriform circuit during feedback inhibition acting on principal cells and is not directly inherited from OB (though it depends on its drive). We have edited our text to incorporate the figure above panel (page 4). We now also relate our results with those of Fukunaga and colleagues for the OB gamma generation and discuss the alternative interpretation of inherited gamma (page 9).

Reviewer #2 (Public Review):

This is a very interesting paper, in which the authors describe how respiration-driven gamma oscillations in the piriform cortex are generated. Using a published data set, they find evidence for a feedback loop between local principal cells and feedback interneurons (FBIs) as the main driver of respiration-driven gamma. Interestingly, odour-evoked gamma bursts coincide with the emergence of neuronal assemblies that activate when a given odour is presented. The results argue in favour of a winner-take-all mechanism of assembly generation that has previously been suggested on theoretical grounds.

We thank the reviewer for his/her work and accurate summary of our results.

The article is well-written and the claims are justified by the data. Overall, the manuscript provides novel key insights into the generation of gamma oscillations and a potential link to the encoding of sensory input by cell assemblies. I have only minor suggestions for additional analyses that could further strengthen the manuscript:

We thank the reviewer for the positive appraisal.

1) The authors' analysis of firing rates of FFIs and FBIs combined with TeLC experiments make a compelling case for respiration-driven gamma being generated in a pyramidal cell-FBI feedback mechanism. This conclusion could be further strengthened by analyzing the gamma phase-coupling of the three neuronal populations investigated. One would expect strong coupling for FBIs but not FFIs (assuming that enough spikes of these populations could be sampled during the respiration-triggered gamma bursts). An additional analysis to strengthen this conclusion could be to extract FBI- and FFI spike-triggered gamma-filtered signals. One might expect an increase in gamma amplitude following FBI but not FFI spiking (see e.g., Pubmed ID 26890123).

We thank the reviewer for the comment. To address this point, we first computed spike-coupling strength (by means of the Mean Vector Length – MVL) for each neuronal subtype. As shown below, we did not find major differences in MVL values across subtypes (if anything, the FBIs actually displayed the lowest MVL, though it should be cautioned that this metric is sensible to sample size, which differed among subtypes):

Of note, this result also translated to spike-triggered gamma-filtered signals, with FBIs having the lowest average. We don’t however believe these findings speak against a major role of FBIs in giving rise to field gamma, since it is expected that inhibited neurons will highly phase-lock to gamma (while more active neurons during gamma would show lower phase-locking). Nevertheless, we also computed the spike-triggered gamma amplitude envelope for all three neuronal subtypes. This analysis showed that gamma envelopes closely followed FBI spikes (and not FFIs or EXC cells), and thus this new result reinforces the idea that FBIs trigger gamma oscillations. This plot is now part of an inset of Figure 1G (described on page 5).

2) The authors utilize the neurons' weight in the first PC to assign them to odour-related assemblies. This method convincingly extracts an assembly for each odour (when odours are used individually), and these seem to be virtually non-overlapping. It would be informative to test whether a similar clear separation of the individual assemblies could be achieved by running the analysis on all odours simultaneously, perhaps by employing a procedure of assembly extraction that allows to deal with overlapping assembly membership better than a pure PCA approach (as used for instance in the work cited on page 11, including the authors' previous work)? I do not doubt the validity of the authors' approach here at all, but the suggested additional analysis might allow the authors to increase their confidence that individual neurons contribute mostly to an assembly related to a single odour.

We thank the reviewer for the pertinent comment. In order to address it, we ran the ICA-based approach to detect cell assemblies (Lopes-dos-Santos et al., 2013) using the spike time series of all odors concatenated. The concatenation included time windows around the gamma peak (100-400 ms after inhalation start). We chose this window to prevent the ICA from picking temporal features of the response as different ICs instead of the spiking variations caused by the different odors. As a reference, we also calculated ICA for each odor independently during the gamma peak.

We found that the results obtained from ICA computed using concatenated data from all odors show important resemblances to those from the single ICA per odor approach. For instance, we get similar sparsity and cell assembly membership (Figure 6-figure supplement 1A), orthogonality (Figure 6-figure supplement 1B), and odor specificity (Figure 6-figure supplement 1C) in the ICs loadings through both approaches. Noteworthy, the average absolute IC correlation between the six odors (computed separately) and the six first ICs (computed from the combined odor responses) were similar across animals and showed no significant differences (Figure 6-figure supplement 1C).

We also directly tested odor selectivity and separation in the concatenated data approach by computing each odor’s mean assembly activity (i.e., “IC projection”). Regarding the former, we found that most assemblies coded for 1 or 2 odors (Figure 6-figure supplement 1D). Regarding the diversity of representations for the sampled neurons, we assessed odor separation by examining to which odor each IC is activated the most. Under this framework, we get that, on average, the first 6 ICs encode three to five different odors (Figure 6-figure supplement 1E).

We have included this result as a new Figure 6-figure supplement 1 and mention it on page 8. Of note, we have also performed all of our previous assembly analyses (i.e., Figure 6) using ICA instead of PCA to be consistent throughout the manuscript and allow the reader to compare with the new supplementary figure. This led to a new and enhanced version of Figure 6.

3) Do the authors observe a slow drift in assembly membership as predicted from previous work showing slowly changing odour responses of principal neurons (Schoonover et al., 2021)? This could perhaps be quantified by looking at the expression strengths of assemblies at individual odour presentations or by running the PCA separately on the first and last third of the odour presentations to test whether the same neurons are still 'winners'.

We thank the reviewer for calling our attention to this point. We note, however, that the representation drift observed by Schoonover et al. occurred along several days of recordings, i.e., at a much slower time scale than the single-day recordings we analyzed here (of note, Schoonover et al. observed no drift within the same day [their Fig 2a]). But irrespective of this, we believe that the data at hand does not allow for a confident analysis of possible drifts. This is because each odor was only presented ~12 times; so, further subdividing the data into subsets of only 4 trials would not render a reliable analysis, unfortunately.

4) Does the winner-take-all scenario involve the recruitment of specific sets of FBIs during the activation of the individual odour-selective assemblies? The authors could address this by testing whether the rate of FBIs changes differently with the activation of the extracted assemblies.

Within each recording session, the number of recorded FBIs is very low, on average 3.6 FBIs per recording session. Thus, unfortunately such interesting analysis cannot be confidently performed.

5) Given the dependence on local gamma oscillations, one might expect that odour-selective assemblies do not emerge in the TeLC-expressing hemisphere. This could be directly tested in the existing data set.

We are thankful for the comment. We followed the reviewer's suggestion and analyzed odor assemblies in TeLC recordings, comparing the ipsilateral hemisphere (infected) with the contralateral one. Interestingly, we find an increased correlation of assembly weights across odors, suggesting that the formation/segregation of odor-selective assemblies is hindered when the principal cell synapses are abolished. This assembly selectivity reduction co-occurred as the number of losing neurons decreased, and the inhibition of the latter was also reduced. Consequently, decoding accuracy significantly decreased during the 150-250 ms window in the infected TeLC hemisphere compared to the contralateral cortex.

Therefore, we believe these new results support the role of gamma oscillations in segregating cell assemblies and generating a sparse orthogonal odor representation. These findings are now included as new panels of Figure 6 and Figure 7 and discussed on page 8.

Author Response

Reviewer #1 (Public Review):

By studying the effect of Treg depletion in a CD8+ T cell-dependent diabetes model the group around Ondrej Stepanek described that in the absence of Treg cells antigen-specific CD8+ OT-I T cells show an activated phenotype and accelerate the development of diabetes in mice. These cells - termed KILR cells - express CD8+ effector and NK cell gene signatures and are identified as CD49d- KLRK1+ CD127+ CD8+ T cells. The authors suggest that the generation of these cells is dependent on TCR stimulation and IL-2 signals, either provided due to the absence of Treg cells or by injection of IL-2 complexed to specific antiIL-2 mAbs. In vivo, these cells show improved target cell killing properties, while the authors report improved anti-tumor responses of combination treatments with doxorubicin combined with IL-2/JES6 complexes. Finally, the authors identified a similar human subset in publicly available scRNAseq datasets, supporting the translational potential of their findings.

The conclusions are mostly well supported, except for the following two considerations:

We are happy for the positive overall evaluation of our manuscript by both reviewers and we are thankful for their specific insightful comments, which helped us to improve the manuscript.

1) From Fig. 4A and B it is not conclusively shown, that Tregs limit IL-2 necessary for the expansion of OT-I cells and subsequent induction of diabetes. An IL-2 depletion experiment (e.g. with combined injection of the S4B6 and JES6-1 antibodies) would further strengthen this claim. Along these lines, the authors claim "IL-2Rα expression on T cells can be induced by antigen stimulation or by IL-2 itself in a positive feedback loop [20]. Accordingly, downregulation of IL-2Rα in OT-I T cells in the presence of Tregs might be a consequence of the limited availability of IL-2.". The cited reference 20 did observe CD25 upregulation by IL-2 on T cells but the observed effect might only be caused by upregulation of CD25 on Treg cells, which increases the MFI for the whole T cell population. Did the authors observe significant upregulation of CD25 on effector CD4+ and CD8+ T cells in their experiments with IL-2/S4B6 or IL-2/JES6 treatment?

We added another reference to support our claim (Sereti, I., et al., Clin Immunol, 2000. 97(3): p. 266-76.). Along this line, we also observed that addition of IL-2 in vitro leads to IL-2Rα upregulation on CD8+ T cells (shown in Fig. 4C), which was IL-2Rα level was lower if Tregs were present. We also observed upregulation of IL-2Rα in vivo upon the stimulation of OT-I T cells with OVA and IL-2ic, which is now shown in the Fig. S6C of the revised manuscript.

To further explore if Tregs limit expansion of OT-I and diabetes progression via IL-2 limitations, we performed the proposed experiment using a combined injection of S4B6 and JES6-1 anti-IL-2 antibodies. At the beginning, we were skeptical that we could completely block the IL-2 using this approach for the following reasons. First, IL-2 is produced locally in the spleen and lymph nodes and might not be easily accessible for the antibodies for a complete block. Second, IL-2 has a relatively short turnover and is continuously produced, but the half-life of the injected antibodies is unknown, which questions the duration of such a block. Third, it is possible that some IL-2 molecules would bound only to one of the two antibodies, which will make it a hyper-stimulating immune-complex, instead of neutralizing it.

Anyway, we were curious enough to perform this experiment. We used a condition that based on our experience leads to diabetes manifestation in Tregs depleted, but not in Treg replete mice (10 k OT-I T cells, OVA + LPS immunization). One additional group of Treg-depleted mice received a single dose of S4B6 and JES6-1 anti-IL-2 (200 µg of each antibody per mouse). We observed that this IL-2 blocking delayed, but not prevented the development of diabetes in most animals (Fig. 1 below).

Overall, we believe that this experiment is rather supporting our conclusions concerning the importance of IL-2, although the effect is only partial. However, we decided not to include this experiment in the manuscript, because we do not have the evidence about how efficient the IL-2 blocking was (see above), which makes the interpretation difficult. Because the reviews and the point-by-point response is public in eLife, we believe that showing the data here is appropriate.

Figure 1. Role of IL-2 blocking on the development of experimental diabetes. Two independent experiments were performed. Statistical significance was calculated using Log-rank (Mantel-Cox) test for survival, and Kruskal-Wallis test for blood glucose (p-value is shown in italics).

2) The anti-tumor efficacy of KILR cells is intriguing but currently, it is unclear if it is indeed mediated by KILR cells. Have KILR cells been identified by flow cytometry in the BCL1 and B16F10 models treated with doxorubicin and IL-2/JES6? Were specific KILR cell depletion studies conducted, e.g. with an anti-KLRK1 depleting antibody? Additional experiments addressing these questions would be desirable to further support the authors' claims.

We are thankful to both reviewers for their similar comments concerning the analysis of CD8+ T cells in the tumor model. Addressing these comments lead to very useful data and significantly improved our manuscript.

We performed the analysis of splenic CD8+ T cells in the BCL1 leukemia model (spleen is the major site of the leukemic cells in this model). We observed that KLRK1+ T cells represented almost half of CD8+ T cells in mice treated with DOX+IL-2, which was much higher frequency than in the control and DOX-only treated mice. Although not all KLRK1+ cells were bona fide KILR cells, the frequencies of KLRK1+ IL-7R+ and KLRK1+ CD49d- cells were also strongly elevated in the Dox+IL-2ic treated mice. Overall, the survival of DOX+IL-2ic treated mice correlated with the frequencies of KILR T cells and KLRK1+ T cells. Moreover, GZMB was almost exclusively expressed by KLRK1+ T cells. We are showing these data in Fig. 7C and Fig. S7B in the revised manuscript.

In the B16 melanoma model, we analyzed CD8+ T cells in the spleens and also in the tumors. We observed a huge population of KLRK1+ GZMB+ CD8+ T-cell population in the spleen of DOX+IL-2ic-treated mice, but not in the untreated or DOX-only treated mice (Fig. 7F). Both KLRK1+ CD49d+ and KLRK1+ CD49d- CD8+ T cells were substantially more frequent in the DOX+IL-2ic-treated, but not in the untreated or DOX-only treated mice (Fig. S7F). In the tumor, the KLRK1+ CD49d- CD8+ T cells were found at large numbers only in the DOX+IL-2ic-treated mice (Fig. 7G). Moreover, these KLRK1+ CD49d- CD8+ T cells expressed high levels of IL-7R and GZMB only in DOX+IL-2ic-treated, but not in untreated and DOX-only treated mice (Fig. 7H).

We believe that these new data provide evidence that the combination of immunogenic chemotherapy with IL-2 treatment induced KILR cells in the spleens and in the tumors and that this correlates with the better survival.

Because the majority of non-naïve CD8+ T cells (and vast majority of GZMB+ CD8+ T cells) in the spleens and tumors of the tumor-bearing mice treated with DOX+IL-2ic were KLRK1+ and because we have shown that the protective effect of the DOX+IL-2ic therapy is largely CD8+ T cell-dependent, we did not find it essential to perform the depletion of KLRK1+ T-cells. We believe that it is almost inevitable that the depletion of KLRK1+ T cells would lead to increased tumor growth as it would probably deplete the majority of antigenspecific CD8+ T cells, mimicking the overall CD8+ T cell depletion. Moreover, we do not have this protocol established.

Reviewer #2 (Public Review):

In this study, the authors determine the superior cell killing abilities of KLRK1+ IL7R+ (KILR) CD8+ effector T cells in experimental diabetes and tumor mouse model. They also provide evidence that Tregs suppress the formation of this previously uncharacterized subset of CD8+ effector T cells by limiting IL-2.

Strength and Limitation

This study focuses on the relationship between Tregs and CD8+ T cells. They used different experimental diabetes mouse models to reveal that Tregs suppress the CD8+ effector T cells by limiting IL-2. They also found a unique subset of KLRK1+ IL7R+ (KILR) CD8+ effector T cells with superior cell killing abilities through single-cell sequencing, but killing abilities could be inhibited by Tregs. They also tested their theory in in vivo tumor model. The data, in general, support the conclusions; however, some issues need to be fully addressed, as detailed below.

We are happy for the positive overall evaluation of our manuscript by both reviewers and we are thankful for their specific insightful comments, which helped us to improve the manuscript.

1) This study used the concentration of urine glucose as the standard for diabetes ({greater than or equal to} 1000 mg/dl for two consecutive days). However, multiple reasons may lead to a high level of urine glucose. As a type I diabetes mouse model, authors could use immunohistological analysis of islet to show the proportion of T cells and islet cells in islet, which can display the geographic distribution of immune cells, severity and histology structure of damaged pancreas islet directly. If possible, different subsets of immune cells, especially CD4 vs CD8+ cells should be stained for their location.

We added the histological examination of the pancreas in control, DEREG-, and DEREG+ mice using contrast H&E staining and immuno-fluorescence (Fig. 1D-E in the revised manuscript). We observed that the high glucose and blood levels are preceded by the destruction of the pancreatic islets (morphology and decreased insulin production) as well as by the infiltration of the islets with immune cells including CD4+ and CD8+ T cells.

2) This article shows that KILR effector CD8+ T cells have strong cytotoxic properties. However, they do not describe the potential proliferation ability vs apoptosis of this subset from islets.

We analyzed the proliferation (KI67 expression) and apoptosis (Annexin V, cleaved Caspase 3) in T cells isolated from the pancreas of DEREG- and DEREG+ mice on day 4 after the induction of diabetes using flow cytometry (Figure 2 below). We did not observe any differences between DEREG- and DEREG+ mice or among different subsets of OT-I T cells in the DEREG+ mice. Essentially, all T cells were proliferative (KI67+) and there was a very low percentage of Annexin V or cleaved Caspase 3 positive cells.

Figure 2. Lymphocytes were isolated from the pancreas of DEREG- RIP.OVA and DEREG+ RIP.OVA mice on day 4 after the induction of diabetes, and analyzed using flow cytometry. Two independent experiments were performed. Gated on OT-I T cells. Top: proliferation rate based on Ki-67 staining. Representative histogram and MFI (median is shown). Middle: Apoptosis rate based on Annexin V staining. Representative histogram shows Annexin V staining in three populations of OT-I T cells from DEREG+ mouse (“AE” - CD49d+ KLRK1-, “++” - CD49d+ KLRK1+, KILR - CD49d- KLRK1+), total OT-I T cells from DEREG-, and a positive control: WT CD8+ T cells treated with hydrogen peroxide. Middle right: Percentage of Annexin V+ cells and MFI (median is shown). Bottom: Apoptosis rate based on cleaved Caspase 3 staining. Representative dot plots show cleaved Caspase 3 staining of OT-I T cells from DEREG+, DEREG-, and a positive control: WT CD8+ T cells treated with hydrogen peroxide. Bottom right: percentage of cleaved Caspase 3+ cells (median is shown).

However, we found question concerning proliferation and apoptosis of KILR cells interesting and worth further investigation. For this reason, we assessed the proliferation, survival, and phenotypic stability of naïve, KILR, and effector T cells by their competitive transfer into CD3ε-/- mice. The phenotype of all these three subsets remained stable for 4 days (Fig. 6F), documenting that KILR cells are not just a very transient stage. Moreover, the KILR cells were ~2 fold more abundant then effector cells 3 days after their 1:1 cotransfer into CD3ε-/- mice (Fig. 6G, Fig. 6SE). This was probably caused by their slight advantages in both proliferation and survival (Fig. 6SF-G).

3) Figure 7 shows that the antitumor efficacy of IL-2 depends on CD8+ T cells. But in this part, there is no data to show the change of KLRK1+ IL7R+ CD8+ effector T cells in tumor tissue. Therefore, the article needs to add more data to verify that IL-2 enhances antitumor ability via KLRK1+ IL7R+ CD8+ effector T cells.

We are thankful to both reviewers for their similar comments concerning the analysis of CD8+ T cells in the tumor model. Addressing these comments lead to very useful data and significantly improved our manuscript.

We performed the analysis of splenic CD8+ T cells in the BCL1 leukemia model (spleen is the major site of the leukemic cells in this model). We observed that KLRK1+ T cells represented almost half of CD8+ T cells in mice treated with DOX+IL-2, which was much higher frequency than in the control and DOX-only treated mice. Although not all KLRK1+ cells were bona fide KILR cells, the frequencies of KLRK1+ IL-7R+ and KLRK1+ CD49d- cells were also strongly elevated in the Dox+IL-2ic treated mice. Overall, the survival of DOX+IL-2ic treated mice correlated with the frequencies of KILR T cells and KLRK1+ T cells. Moreover, GZMB was almost exclusively expressed by KLRK1+ T cells. We are showing these data in Fig. 7C and Fig. S7B in the revised manuscript.

In the B16 melanoma model, we analyzed CD8+ T cells in the spleens and also in the tumors. We observed a huge population of KLRK1+ GZMB+ CD8+ T-cell population in the spleen of DOX+IL-2ic-treated mice, but not in the untreated or DOX-only treated mice (Fig. 7F). Both KLRK1+ CD49d+ and KLRK1+ CD49d- CD8+ T cells were substantially more frequent in the DOX+IL-2ic-treated, but not in the untreated or DOX-only treated mice (Fig. S7F). In the tumor, the KLRK1+ CD49d- CD8+ T cells were found at large numbers only in the DOX+IL-2ic-treated mice (Fig. 7G). Moreover, these KLRK1+ CD49d- CD8+ T cells expressed high levels of IL-7R and GZMB only in DOX+IL-2ic-treated, but not in untreated and DOX-only treated mice (Fig. 7H).

We believe that these new data provide evidence that the combination of immunogenic chemotherapy with IL-2 treatment induced KILR cells in the spleens and in the tumors and that this correlates with the better survival.

4) It is unclear why the authors chose Dox to combine with IL-2/JES6. The authors should provide a more rational introduction to bridge such a combination. Authors should also explain the reason why there is no antitumor effect of IL-2/JES6 treatment alone.

The experiments with OT-I mice showed that the formation of KILR cells required both the antigenic stimulation and IL-2 signals. We believe that there is only very week antigenic stimulation by the tumor itself. For this reason, we combined the treatment with the chemotherapy Doxorubicin, which is known to induce immunogenic cell death of the tumor cells (e.g., Casares et al. 2005, PMID: 16365148). We believe that doxorubicin induces the death of (some) tumor cells and the release and presentation of their tumorspecific antigens. Without it, the tumor are simply too “cold” to induce sufficient T-cell response. We emphasized this in the revised version of the manuscript.

Importantly, some of us observed a similar effect of IL-2ic in a combination with check-point blockade therapy (without chemotherapy) in a different tumor model, which documents that the chemotherapy is not essential for this effect (unpublished data).

Author Response

Reviewer #1 (Public Review):

Point 1: Many of the initial analyses of behavior metrics, for instance predicting reaction times, number of fixations, or fixation duration, use value difference as a regressor. However, given a limited set of values, value differences are highly correlated with the option values themselves, as well as the chosen value. For instance, in this task the only time when there will be a value difference of 4 drops is when the options are 1 and 5 drops, and given the high performance of these monkeys, this means the chosen value will overwhelmingly be 5 drops. Likewise, there are only two combinations that can yield a value difference of 3 (5 vs. 2 and 4 vs 1), and each will have relatively high chosen values. Given that value motivates behavior and attracts attention, it may be that some of the putative effects of choice difficulty are actually driven by value.

To address this question, we have adapted the methods of Balewski and colleagues (Neuron, 2022) to isolate the unique contributions of chosen value and trial difficulty to reaction time and the number of fixations in a given trial (the two behaviors modulated by difficulty in the original paper). This new analysis reveals a double dissociation in which reaction time decreases as a function of chosen value but not difficulty, while the number of fixations in a trial shows the opposite pattern. Our interpretation is that reaction time largely reflects reward anticipation, whereas the number of fixations largely reflects the amount of information required to render a decision (i.e., choice difficulty). See lines 144-167 and Figure 2.

Point 2: Related to point 1, the study found that duration of first fixations increased with fixated values, and second (middle) fixation durations decreased with fixated value but increased with relative value of the fixated versus other value. Can this effect be more concisely described as an effect of the value of the first fixated option carrying over into behavior during the second fixation?

This is a valid interpretation of the results. To test this directly, we now include an analysis of middle fixation duration as a function of the not-currentlyviewed target. Note that the vast majority of middle fixations are the second fixation in the trial, and therefore the value of the unattended target is typically the one that was viewed first. The analysis showed a negative correlation between middle fixation duration and the value of the unattended target which is consistent with the first fixated value carrying over to the second fixation. See lines 243-246.

Point 3: Given that chosen (and therefore anticipated) values can motivate responses, often measured as faster reaction times or more vigorous motor movements, it seems curious that terminal non-decision times were calculated as a single value for all trials. Shouldn't this vary depending at least on chosen values, and perhaps other variables in the trial?

In all sequential sampling model formulations we are aware of, nondecision time is considered to be fixed across trial types. Examples can be found for perceptual decisions (e.g., Resulaj et al., 2009) and in the “bifurcation point” approach used in the recent value-based decision study by Westbrook et al. (2020).

To further investigate this issue, we asked whether other post-decision processes were sensitive to chosen value in our paradigm. To do so, we measured the interval between the center lever lift and the left or right lever press, corresponding to the time taken to perform the reach movement in each trial (reach latency). We then fit a mixed effects model explaining reach latency as a function of chosen value. While the results showed significantly faster reach latencies with higher chosen values, the effect size was very small, showing on average a ~3ms decrease per drop of juice. In other words, between the highest and lowest levels of chosen value (5 vs. 1), there is only a difference of approximately 12ms. In contrast, the main RT measure used in the study (the interval between target onset and center lever lift) is an order of magnitude more sensitive to chosen value, decreasing ~40ms per drop of juice. These results are shown in Author response image 1.

Author response image 1.

This suggests that post-decision processes (NDT in standard models and the additive stage in the Westbrook paper) vary only minimally as a function of chosen value. We are happy to include this analysis as a supplemental figure upon request.

Point 4: The paper aims to demonstrate similarities between monkey and human gaze behavior in value-based decisions, but focuses mainly on a series of results from one group of collaborators (Krajbich, Rangel and colleagues). Other labs have shown additional nuance that the present data could potentially speak to. First, Cavanaugh et al. (J Exp Psychol Gen, 2014) found that gaze allocation and value differences between options independently influence drift rates on different choices. Second, gaze can correlate with choice because attention to an option amplifies its value (or enhances the accumulation of value evidence) or because chosen options are attended more after the choice is implicitly determined but not yet registered. Westbrook et al. (Science, 2020) found that these effects can be dissociated, with attention influencing choice early in the trial and choice influencing attention later. The NDTs calculated in the present study allot a consistent time to translating a choice into a motor command, but as noted above don't account for potential influences of choice or value on gaze.

The two-stage model of gaze effects put forth by Westbrook et al. (2020) is consistent with other observations of gaze behavior and choice (i.e., Thomas et al., 2019, Smith et al., 2018, Manohar & Husain, 2013). In this model, gaze effects early in the trial are best described by a multiplicative relationship between gaze and value, whereas gaze effects later in the trial are best described with an additive model term. To test the two-stage hypothesis, Westbrook and colleagues determined a ‘bifurcation point’ for each subject that represented the time at which gaze effects transitioned from multiplicative to additive. In our data, trial durations were typically very short (<1s), making it difficult to divide trials and fit separate models to them. We therefore took at different approach: We reasoned that if gaze effects transition from multiplicative to additive at the end of the trial, then the transition point could be estimated by removing data from the end of each trial and assessing the relative fit of a multiplicative vs. additive model. If the early gaze effects are predominantly multiplicative and late gaze effects are additive, the relative goodness of fit for an additive model should decrease as more data are removed from the end of the trial. To test this idea, we compared the relative model fit of an additive vs. multiplicative models in the raw data, and for data in which successively larger epochs were removed from the end of the trial (50, 100, 150, 200, 300, and 400ms). The relative fit was assessed by computing the relative probability that each model accurately reflects the data. In addition, to identify significant differences in goodness of fit, we compared the WAIC values and their standard errors for each model (Supplemental File 3). As shown in Figure 4, the relative fit probability for both models is nonzero in the raw data 0 truncation), indicating that a neither model provides a definitive best fit, potentially reflecting a mixture of the two processes. However, the relative fit of the additive model decreases sharply as data is removed, reaching zero at 100ms truncation. 100ms is also the point at which multiplicative models provide a significantly better fit, indicated by non-overlapping standard error intervals for the two models (Supplemental File 3). Together, this suggested that the transition between early- and late-stage gaze effects likely occurs approximately 100ms before the RT.

To minimize the influence of post-decision gaze effects, the main results use data truncated by 100ms. However, because 100ms is only an estimate, we repeated the main analyses over truncation values between 0 and 400ms, reported in Figure 6 - figure supplement 1 & Figure 7 - figure supplement 1. These show significant gaze duration biases and final gaze biases in data truncated by up to 200ms.

Reviewer #2 (Public Review):

Recommendation 1: The only real issue that I see with the paper is fairly obvious: the authors find that the last fixations are longer than the rest, which is inconsistent with a lot of the human work. They argue that this is due to the reaching required in this task, and they take a somewhat ad-hoc approach to trying to correct for it. Specifically, they take the difference between final and non-final, second fixations, and then choose the 95th percentile of that distribution as the amount of time to subtract from the end of each trial. This amounts to about 200 ms being removed from the end of each trial. There are several issues with this approach. First, it assumes that final and non-final fixations should be the same length, when we know from other work that final fixations are generally shorter. Second, it seems to assume that this 200ms is "the latency between the time that the subject commits to the movement and the time that the movement is actually detected by the experimenter". However, there is a mismatch between that explanation and the details of the task. Those last 200ms are before the monkey releases the middle lever, not before the monkey makes a left/right choice. When the monkey releases the middle lever, the stimuli disappear and they then have 500ms to press the left or right lever. But, the reaction time and fixation data terminate when the monkey releases the middle lever. Consequently, I don't find it very likely that the monkeys are using those last 200ms to plan their hand movement after releasing the middle lever.

Thanks for the opportunity to clarify these points. There are three related issues:

First, with regards to fixation durations, in the updated Figure 3 we now show durations as a function of both the absolute order in the trial (first, second, third, fourth, etc.) and the relative order (final/nonfinal). We find that durations decrease as a function of absolute order in the trial, an effect also seen in humans (see Manohar & Husain, 2013). At the same time, while holding absolute order constant, final fixations are longer than non-final fixations. To explain the discrepancy with human final fixation durations, we note that monkeys make many fewer fixations per trial (~2.5) than humans do (~3.7, computed from publicly available data from Krajbich et al., 2010.) This means that compared to humans, monkeys’ final fixations occur earlier in the trial (e.g., second or third), and are therefore comparatively longer in duration. Note that studies with humans have not independently measured fixation durations by absolute and relative order, and therefore would not have detected the potential interaction between the two effects.

Second, the comment suggests that the final 200ms before lever lift is not spent planning the left/right movement, given that the monkeys have time after the lever lift in which to execute the movement (400 or 500ms, depending on the monkey). The presumption appears to be that 400/500ms should be sufficient to plan a left/right reach. However, we think that these two suggestions are unlikely, and that our original interpretation is the most plausible. First, the 400/500ms deadline between lift and left/right press was set to encourage the monkeys to complete the reach as fast as possible, to minimize deliberations or changes of mind after lifting the lever. More specifically, these deadlines were designed so that on ~0.5% of trials, the monkeys actually fail to complete the reach within the deadline and fail to obtain a reward. This manipulation was effective at motivating fast reaches, as the average reach latency (time between lift and press) was 165 SEM 20ms for Monkey K, and 290 SEM 100ms for Monkey C.

Therefore, given the time pressure imposed by the task, it is very unlikely that significant reach planning occurs after the lever lift. In addition to these empirical considerations, the idea that the final moments before the RT are used for motor planning is a standard assumption in many theoretical models of choice (including sequential sampling models, see Ratcliff & McKoon 2008, for review), and is also well-supported by studies of motor control and motor system neurophysiology. Based on these, we think the assumption of some form of terminal NDT is warranted.

Third, we have changed our method for estimating the NDT interval. In brief we sweep through a range of NDT truncation values (0-400ms) and identify the smallest interval (100ms) that minimizes the contribution of “additive” gaze effects, which are thought to reflect late-stage, post-decision gaze processes. See the response to Point 4 for Reviewer 1 above, Figure 4 and lines 267-325 in the main text. In addition, we report all of the major study results over a range of truncation values between 0 and 400ms.

Author Response

Reviewer #1 (Public Review):

This paper describes the neural activity, measured by intrinsic optical imaging in reach-to-grasp, and reach-only conditions in relation to the Intra-cortical micro stimulation maps. The paper mostly describes a relatively unique and potentially useful data set. However, in the current version, no real hypotheses about the organization of M1 and PMd are tested convincingly. For example, the claim of "clustered neural activity" is not tested against any quantifiable alternative hypothesis of non-clustered activity, and support for this idea is therefore incomplete.

The combination of intrinsic optical imaging and intra-cortical micro-stimulation of the motor system of two macaque monkeys promised to be a unique and highly interesting dataset. The experiments are carefully conducted. In the analysis and interpretation of the results, however, the paper was disappointing to me. The two main weaknesses in my mind were:

a) The alternative hypotheses depicted in Figure 1B are not subjected to any quantifiable test. When is an activity considered to be clustered and when is it distributed? The fact that the observed actions only activate a small portion of the forelimb area (Figure 5G, H) is utterly unconvincing, as this analysis is highly threshold-dependent. Furthermore, it could be the case that the non-activated regions simply do not give a good intrinsic signal, as they are close to microvasculature (something that you actually seem to argue in Figure 6b). Until the authors can show that the other parts of the forelimb area are clearly activated for other forelimb actions (as you suggest on line 625), I believe the claim of cluster neural activity stands unsupported.

We appreciate the reviewer’s concerns and we have made several revisions.

(1) The two panels in Fig 1B should have been presented as potential outcomes as opposed to hypotheses in need of quantifiable testing. We revised the Introduction (line 105-111) and the Results (line 149-152) accordingly.

(2) We agree that the thresholding procedure adopted in the original submission could have impacted the spatial measurements of cortical activity (i.e., Fig 5G-H in original submission). We have completely revised the thresholding procedure and it is now based on statistical comparisons that include all trials (instead of thresholding by number of sessions in the original submission). Thus, the thresholded maps in Fig 5G & 5J are now obtained from pixel-by-pixel comparisons (t-tests, p<1e-4) between frames acquired post-movement and frames acquired before movement. Nevertheless, even with this relatively relaxed threshold, the largest activity maps overlapped <40% of the forelimb representations.

It is important to note that major vessels were excluded from the thresholded map and from the motor map. Thus, uncertainty about imaging in and around vessels was likely not a factor in the calculated overlap between thresholded maps and the motor map.

(3) We agree that showing activation in other parts of the forelimb representations in response to action other than reach-to-grasp would have supported some of the arguments that we previously put forth. Unfortunately, we do not have the supporting data and obtaining it would take months/years. We have therefore expanded the Discussion to include limitations of the behavioral task (line 439-443).

b) The most interesting part of the study (which cannot be easily replicated with human fMRI studies) is the correspondence between the evoked activity and intra-cortical stimulation maps. However, this is impeded by the subjective and low-dimensional description of the evoked movement during stimulation (mainly classifying the moving body part), and the relatively low-dimensional nature (4 conditions) of the evoked activity.

We agree with the reviewer on all accounts. We expanded the Discussion to consider the low dimensionality of the motor maps and the behavioral task (line 439-449).

Measuring cortical activity in a variety of motor tasks would likely have provided additional insight about movement-related cortical activity. Nevertheless, including additional tasks, even if it were possible to do so in the same monkeys, would have delayed study completion by months/years. The hidden challenge of the experimental design is that each monkey is trained to not move for many seconds to minimize contamination of ISOI signals. For example, from trial initiation to Go Cue, the monkey must hold its hand in the start position for 5 seconds. Similarly, after movement completion, the monkey must hold its hand in the start position for another 5 seconds. In between successful trials, a monkey must wait for ~12 seconds before it can initiate a new trial. These durations are >1 order of magnitude longer than in electrophysiological studies in comparable tasks. Achieving consistent task performance with the long durations used here, took months of daily training. Moreover, our monkeys typically run out of steam after ~60-70 min of working on the task. This forces us to limit the overall number of task conditions tested in a session, to obtain a large enough number of trials from each condition.

c) Many details about the statistical analysis remain unclear and seem not well motivated.

We address the reviewer’s specific concerns.

Reviewer #2 (Public Review):

Chehade and Gharbawie investigated motor and premotor cortex in macaque monkeys performing grasping and reaching tasks. They used intrinsic signal optical imaging (ISOI) covering an exceedingly large field-of-view extending from the IPS to the PS. They compared reaching and fine/power-grip grasping ISOI maps with "motor" maps which they obtained using extensive intracranial microstimulation. The grasping/reaching-induced activity activated relatively isolated portions of M1 and PMd, and did not cover the entire ICM-induced 'motor' maps of the upper limbs. The authors suggest that small subzones exist in M1 and PMd that are preferentially activated by different types of forelimb actions. In general, the authors address an important topic. The results are not only highly relevant for increasing our basic understanding of the functional architecture of the motor-premotor cortex and how it represents different types of forelimb actions, but also for the development of brain-machine interfaces. These are challenging experiments to perform and add to the existing yet complementary electrophysiology, fMRI, and optical imaging experiments that have been performed on this topic - due to the high sensitivity and large coverage of the particular IOSI methods employed by the authors. The manuscript is generally well written and the analyses seem overall adequate - but see below for some additional analyses that should be done. Although I'm generally enthusiastic about this manuscript, there are two major issues that should be clarified. These major questions relate mainly to potential thresholding issues and clustering issues.

Major:

1) The main claim of the authors is that specific forelimb actions activate only a small fraction of what they call the motor map (i.e., those parts of M1/PMd that evoke muscle contractions upon ICM). The action-related activity is measured by ISOI. When looking a the 'raw' reflectance maps, it is rather clear that relatively wide portions of the exposed cortex are activated by grasping/reaching, especially at later time points after the action. In fact, another reading of the results may be that there are two zones of 'deactivation' that split a large swath of motor-premotor cortex being activated by the grasping/reaching actions. (e.g. at 6 seconds after the cue in Fig 3A, 5A). At first sight, the 'deactivated' regions seem to be located in the cortex representing the trunk/shoulder/face - hence regions not necessarily activated (or only weakly) during the grasping/reaching actions. If true, this means that most of the relevant M1/PMd cortex IS activated during the latter actions - opposing the 'clustering' claims of the authors. This raises the question of whether the 'granularity' claimed by the authors is

a. threshold dependent. In this context, the authors should provide an analysis whereby 'granularity' is shown independent of statistical thresholds of the ISOI maps.

We appreciate the reviewer’s concerns and have completely revised the analyses central to Fig 5. We believe that the figure now contains evidence from both thresholded and unthresholded ISOI data in support of limited spatial extent of cortical activation (i.e., “granularity” in the reviewer’s comments).

For evidence from unthresholded ISOI data, we examined reflectance change time courses from different size ROIs (line 764-768). (A) Small circular ROIs (0.4 mm radius), which we placed in the M1 hand, M1 arm, and PMd arm, zones (Fig 5B). (B) Large ROI inclusive of the M1 and PMd forelimb representations (Fig 5B). We reasoned that if cortical activity is spatially widespread, then the small and large ROIs would report similar time courses. In contrast, if cortical activity is spatially focal, then activity would be detected in the small ROI time courses but would washed out in the large ROI time courses. Our results support the second possibility (Fig 5C-F). Thus, in the movement conditions, time courses from the small ROIs had a large negative peak after movement completion (Fig C-E). In contrast, the characteristic negative peak was absent in the time courses obtained from the large ROI (Fig 5F).

Separately, we revised our thresholding approach to make those results less sensitive to thresholding effects (more details in our response to the first major point from Reviewer 1). The revised results – thresholded/ binarized maps – are consistent with focal cortical activity. Fig 5G & 5J show activity maps thresholded (t-test, p<0.0001) without correction for multiple comparisons, and therefore represent the least restrictive estimate of the spatial extent of cortical activity. Measurements from these maps showed that significantly active pixels overlapped <40% of the M1 & PMd forelimb representations. We interpret the thresholded results as evidence in support of focal cortical activity.

This raises the question of whether the 'granularity' claimed by the authors is

b. dependent on the time-point one assesses the maps. Given the sluggish hemodynamic responses, it is unclear which part of the ISOI maps conveys the most information relative to the cue and arm/hand movements. I suspect that timepoints > 6 s will reveal even larger 'homogeneous' activations compared to the maps < 6s.

We agree with the reviewer that the lag in hemodynamic signals complicates frame selection. Nevertheless, it is unlikely that cortical activity maps would have been larger at time points >6s from Cue. We provide three supporting arguments.

(1) In the imaging sessions used in Fig 4, we acquired images for 9s per trial and systematically varied Cue onset time. The time courses in Fig 4A-B show that for all Cue onset conditions, the negative peak occurred <6s from Cue. This observation from unthresholded results does not support the notion of greater cortical activity at time points >6s from Cue.

(2) From the same experiment, Fig 4C shows 9 thresholded/binarized maps generated from different time points in relation to Cue. We measured the size of each map (i.e., overlap with the M1/PMd forelimb representations). We present the results in Author response image 1. The largest maps came from an average frame captured +5.8-6.0s from Cue. Those maps are on the diagonal in Fig 4E (top left to bottom right). This result from thresholded data therefore does not support the notion of greater cortical activity at time points >6s from Cue.

Author response image 1.

(3) In all other sessions, we acquired images for 7s per trial (-1.0 to +6.0 s from Cue) without varying Cue onset time. At every time point (100 ms), we measured the size of the thresholded/binarized map in relation to the size of the M1 and PMd forelimb representations. The results are presented in Fig 5I & 5L and indicate that thresholded maps plateau in size by 5.0-5.5 s from Cue. At peak size, the maps overlapped <50% of the M1 and PMd forelimb representations. These result indicates that it is unlikely that we underreported the size of activity maps by not measuring map size beyond 6s from Cue.

In fact, Fig 5F (which is highly thresholded) shows a surprisingly good match between the different forelimb actions, which argues against the existence of small subzones that are preferentially activated by different types of forelimb actions -the main claim of the authors.

Our original proposal should have been more clearly stated. We were proposing that the thresholded maps, which had similar spatial organizations across conditions as the reviewer suggested, reported on subzones tuned for reach-to-grasp actions. Adjacent to those subzones could be other subzones that are preferentially active during other types of forelimb actions (e.g., pulling, pushing, grooming). We could not test this possibility in our study because the behavioral task examined a narrow range of arm and hand actions. We therefore revised the Discussion to state the limitations of our task and to lean more on published work that supports the present proposal (439-443 and 504-508).

2) Related to the previous point, the ROI selections/definitions for the time course analyses seem highly arbitrary. As indicated in the introduction, the clustering hypothesis dictates that "an arm function would be concentrated in subzones of the motor arm zones. Neural activity in adjacent subzones would be tuned for other arm functions." To test this hypothesis directly in a straightforward manner, the authors could use the results from the ICM experiment to construct independent ROIs and to evaluate the ISOI responses for the different actions. In that case, the authors could do a straightforward ANOVA (if the data permits parametric analyses) with ROI, action, and time point (and possibly subject) as factors.

We agree with the reviewer, and we now leverage the ICMS map for guiding ROI placement. All time courses are now derived from 1 of 2 types of ROIs. (1) Small ROIs (0.4 mm radius) placed in zones defined from ICMS (e.g., M1 hand zone). (2) Large ROIs that include the entire forelimb representations in M1 or in PMd (Fig 5B).

Author Response

Reviewer #1 (Public Review):

However, the authors are cautioned to tone down some of the sentences with the human diabetic samples as they rely heavily on extrapolation rather experimental tests.

Thank you for this feedback. We have added an experimental test to support the CellChat results. We found that, in accordance with the CellChat analysis, more macrophage Gas6 expression is observed in diabetic wounds via IF. These data are now included in Figures 3C-D. We have additionally edited the text relating to Figure 3 to indicate that these results are not fully conclusive.

For instance, the antibody inhibition of Axl had minimal effect on the clearance of apoptotic cells in the wound and this would be expected with the redundancy endowed by other TAM receptors.

Thank you for this point. We have made a note of this in the text in lines 289-291.

For instance, in Figure 6, the number of TUNEL+ cells seem to be higher in the IgG samples compared to the anti-Timd4 treatment, but this is not the case in the quantification

Thank you for this comment. We have replaced these with more representative images, which appear in Figure 6A. We also repeated the staining with antibodies for cleaved caspase 3, which appear in Fig. 6 – Fig. supplement 1A, which showed similar results.

Reviewer #2 (Public Review):

I suggest to repeat the quantification of cells containing active caspase-3 with an anticleaved caspase-3 antibody. Here the authors use an antibody recognizing phospho S150 antibody, which is far from generally accepted to be a marker for active caspase-3. It would also be good to quantify the apoptotic cells observed in the sections (Fig 1 I and J) and compare to control treatment on sections. It is not clear from the data presented whether the number of apoptotic cells increases or not in the time frame analyzed since the controls are lacking.

Thank you for this important suggestion. We have repeated the IF staining using an antibody for cleaved caspase 3 (Cell Signaling 9661S) and quantified the apoptotic cells present. We found that apoptotic cells were rare but present at both 24h and 48h after injury, and that significantly more cleaved caspase 3+ cells were present in 48h wounds than 24h wounds. These data are now included in Figure 1H-J and Fig. 1 – Fig. supplement 1F. We have also used this antibody in IF staining in Fig. 5 – Fig. supplement 1B and Fig. 6 – Fig. supplement 1A.

In a FACS analysis (Fig S1 H), the authors show that there is no increase in dead cells in a time frame of 48 hrs. Could it be that the majority of the cells that may have died in vivo, were lost during the procedure of tissue digestions. Dead cells tend to aggregate.

Based on these comments and the inconsistency in these data due to potential technical challenges, we have removed the FACS data quantifying Annexin V. We now include the quantification of cleaved caspase 3 and an efferocytosis assay to analyze the kinetics of efferocytosis.

On line 104 the authors refer to the apoptosis-inducing activity of G0s2. Please, realize that there is little or no in vivo evidence for a role of G0s2 in apoptosis.

Thank you for this helpful comment. We have removed this gene from our analysis and text.

The authors state that Axl is uniquely expressed in DC and fibroblasts (Fig 2). Are the Axlcells positive in panel G (red, Fig 2) that do not stain for the Pdgfra marker (green) then all DCs? Please clarify or show with a triple staining that these cells are indeed DCs.

Thank you for this comment. To clarify, our intention was to show that both DCs and fibroblasts express Axl, not to say conclusively that only DCs and fibroblasts express Axl. Indeed, in Figure 5, we show that a portion of macrophages also express Axl (at day 3), so some of the Axl+ cells in 2G may be macrophages rather than DCs. We have made this more clear in the text in lines 163-166.

In addition, it is not clear to me to what reference level exactly the expression levels are compared in Fig 2A. Is this between the 24 and 48h time points after wounding (as mentioned in the legend)? If so, the analysis may indicate up or down regulation but not necessarily expression or no expression.

Thank you for making this point. The heatmaps display scaled log-normalized mRNA counts for the entire dataset, not a comparison between the two timepoints. We have clarified this in the figure legends.

2) Human diabetic wounds display increased and altered efferocytosis signaling via Axl. This conclusion is solely based on CellChat analysis and should be tuned down or validated.

Thank you for this suggestion. We have experimentally validated this conclusion using IF staining for Gas6. We found that more Gas6 staining in CD68+ macrophages in diabetic foot ulcers when compared to nondiabetic foot wounds. These data are now included in Figure 3C-D.

The authors conclude that anti-Axl treatment leads to healing defects based on lack of granulation tissue and larger scabs, a reduction of fibroblast repopulation and revascularization. The differences in the last two parameters mentioned above are obvious, however the other parameters, as granulation tissue and scabs are less clear to me. Is this quantified in any way? In Fig S4 D there is also a large scab visible in the control treatment image. Therefore, it would be good if these parameters could be better substantiated.

Thank you for this comment. We have edited the text in lines 301-304 to de-emphasize these qualitative changes.

In view of the lack of revascularization, are there differences in the mRNA expression levels of angiogenic factors such as VEGF and others at this time point? Does revascularization occur at later stages?.

Thank you for this helpful suggestion. We have used qPCR to measure Vegfa mRNA expression, and these data are now included in Figure 5I. We found no significant difference in Vegfa expression 5 days after injury.

Based on the FACS analysis the authors claim that there are no differences at the level of DCs. However, the plots shown in Fig 5C do not convincingly show the detection of DC (as boxed in the lower panel). Based on the density plots one would presume this is just the continuation of the CD11b+ population and not a separate CD11c+ population. To get a better view of that, it would be better to show dot plots instead of density plots.

Thank you for this insightful comment. We have created new plots as suggested to demonstrate that this is not exactly the case. In the wound bed, contrary to what we see in blood isolates many times the full separation of populations is elusive and to ensure that we use single stain controls to set the gates. Nonetheless, we provide in Author response image 1 the same data as dot-plots as requested to show that that is not the case, alongside the single stain control to show that the gating strategy is adequate. We do understand and acknowledge that in dissociated tissues sometimes the outlines are not as perfect as what is obtained in immunological samples.

Author response image 1.

Finally, the authors state (line 265-266) that anti-Axl treatment leads to non-significantly increased expression of IL1alpha and IL6 after one day of injury (Fig S4C). If the difference between the control-treated and the anti-Axl-treated group is statistically not significant I would not conclude there is an increase. Please adapt phrasing or include more mice in the experiment (now only 4) to substantiate the observation and clarify whether it is increased or not.

Thank you for this comment. We have altered the text in lines 286-289 to better reflect this.

The authors conclude that overall healing was not affected but that the wound beds appeared more fragile. What is meant with 'appeared more fragile' is not clear. In addition, this seems to me a quite subjective interpretation. What are the objective parameters to come this conclusion?

Thank you for this point. We have altered the text to remove this subjective language.

Similar to inhibition of Axl, inhibition of Timd4 led to a defect in revascularization as witnessed by the absence of CD31 staining. Also in this experiment one can raise similar questions as in the anti-Axl experiment: 1) does revascularization occur at a later timepoint; 2) what about the expression of angiogenic factors?

Thank you for this helpful suggestion. To further investigate the impact of Axl inhibition of angiogenesis, we have assayed for Vegfa by qPCR. We found no significant difference in Vegfa expression 5 days after injury. These data are now included in Figure 5I.

In the anti-Timd4 treated wounds the authors observe more TUNEL-positive cells and conclude that this is due to a defect in efferocytosis. However, the formal experimental proof for this in the current model is lacking. How do the authors exclude the possibility that anti-Timd4 treatment attracts more infiltrating cells that then undergo treatment, or that the treatment with anti-Timd4 leads to more apoptosis of certain cells in the wound bed. What is the nature of these apoptotic cells (neutrophils, T cells, others)? It has been shown that Timd4 can have stimulatory effects on other cells, such as T cells. Could deprivation of Timd4 signaling in certain conditions lead to more dying cells in this model?

Thank you for this insightful comment. To investigate this, we have repeated this experiment with IF staining for cleaved caspase 3 and found similar results, indicating the increase in apoptosis upon Timd4 inhibition (Fig. 6 – Fig. supplement 1A). We have also included text to acknowledge the possibility of an increase in apoptosis in lines 326-327.

Reviewer #3 (public Review)):

They never do show that there is an increase in apoptotic cells in the wounds, which then go down (which would be a sign that the cells are being cleared via efferocytosis. In addition, they are looking for apoptotic cells at very early time points (24-48 hours), times at which large numbers of apoptotic cells would not be expected. As an example, neutrophil infiltration peaks at 24-48 hours and efferocytosis of apoptotic neutrophils would be expected after that. Other types of apoptotic cells would likely be cleared even later. Finally, several of the panels showing apoptotic cells were done with a very small number of samples (1-3 per group) in some cases so it is unclear how rigorous the data are. I would recommend that the authors at the very least soften the wording related to these conclusions and discuss the limitations of their experimental design; ideally data from more samples would be included to provide clear support those statements.

Thank you for raising this important point. In order to support these claims, we have undertaken two additional experiments. Firstly, we have repeated the immunofluorescence staining with a new antibody for activated caspase 3 and quantified the number of apoptotic cells present in 24h and 48h wound beds. We found that apoptotic cells significantly increased in 48h wound beds compared to 24h wounds (Figures 1H and Fig. 1 – Fig. supplement 1F).

We have also undertaken a new experiment to show the temporal regulation of efferocytosis. We injected stained apoptotic neutrophils into 1D, 3D, and 5D wound beds and quantified the stained cells remaining after 1 hour in order to quantify the clearance of cells from the wound bed at different timepoints. We found that significantly more stained cells undergoing efferocytosis remained in 5D wounds, and that the rate of efferocytosis was approximately constant over this timeline. These data are now included in Figures 2H-M.

While we would be interested to determine the identities of cells engaging in efferocytosis of the labeled apoptotic neutrophils, we found that co-staining for additional cell markers was impossible while maintaining the fluorescent labeling on the injected neutrophils.

2) The human RNA-seq data is also quite limited, as non-diabetic wound tissue was all from one patient. Again, this limitation should be acknowledged.

Thank you for this feedback. We have analyzed new data sets that include 5 individuals with diabetic foot ulcers and 4 individuals with non-diabetic wounds. These data are now included in Figure 3.

Also, there are some important published papers by Sashwati Roy's group indicating that there are defects in efferocytosis in diabetic wounds, which may go against what the authors are showing here to some degree. Discussion of the authors' work in relation to these other studies should be discussed.

Thank you for this suggestion. We have included discussion of this work to the text in lines 192193.

3) For anti-Axl and anti-Timd4 experiments, the authors conclude that inhibition of Axl does not affect TUNEL+ cells and that Timd4 does not affect reepithelialization. However, in some cases the sample size was only 3 mice per group when measuring these parameters. That is a very small number of samples to draw conclusions about apoptotic cells or reepithelialization since these parameters are key for the overall conclusions of the experiments. Given that these are key data, it would be important to include more than n=3. Additionally, as stated above, a time point later than 24 h may be necessary to actually see changes in apoptotic cells.

Thank you for this suggestion. We have repeated the staining for apoptotic cells using a new antibody for cleaved caspase 3 and stained wound beds from additional mice. In the anti-Axl experiments, we now show data for cleaved caspase 3 staining of 3- and 5-day wound beds with N=4 (Fig. 5 – Fig. supplement 1B). In the anti-Timd4 experiments, we now have N=6-11 for the TUNEL staining at 5 days after injection and injury (Figure 6B).

4) In Fig 6, there look to be many more TUNEL+ cells in the wound bed of IgG control samples compared to anti-Timd4-treated samples, which contradicts the graph. Perhaps the authors could clarify where they were taking their measurements for panels with image analysis results.

Thank you for this helpful point. We have updated this figure to be more representative of the quantification (Figure 6A-B), as well as repeated the staining with antibodies for cleaved caspase 3 (Fig. 6 – Fig. supplement 1A).

Another question related to this experiment is how it is possible that efferocytosis is so drastically different yet there are no changes in wound healing (this is one reason why a larger sample size for reepithelialization may be critical) - this would seem to suggest that efferocytosis is not important in wound healing, which is confusing. Further discussion on this might be useful.

Thank you for this point. Indeed, we see that there is a defect to revascularization when Timd4 is inhibited (Figure 6E-F), which indicates that efferocytosis is important to normal healing. This is discussed in lines 333-335.

Author response:

Reviewer #1 (Public Review):

Reviewer #1, comment #1: The study is thorough and systematic, and in comparing three well-separated hypotheses about the mechanism leading from grid cells to hexasymmetry it takes a neutral stand above the fray which is to be particularly appreciated. Further, alternative models are considered for the most important additional factor, the type of trajectory taken by the agent whose neural activity is being recorded. Different sets of values, including both "ideal" and "realistic" ones, are considered for the parameters most relevant to each hypothesis. Each of the three hypotheses is found to be viable under some conditions, and less so in others. Having thus given a fair chance to each hypothesis, nevertheless, the study reaches the clear conclusion that the first one, based on conjunctive grid-by-head-direction cells, is much more plausible overall; the hypothesis based on firing rate adaptation has intermediate but rather weak plausibility; and the one based on clustering of cells with similar spatial phases in practice would not really work. I find this conclusion convincing, and the procedure to reach it, a fair comparison, to be the major strength of the study.

Response: Thanks for your positive assessment of our manuscript.

Reviewer #1, comment #2: What I find less convincing is the implicit a priori discarding of a fourth hypothesis, that is, that the hexasymmetry is unrelated to the presence of grid cells. Full disclosure: we have tried unsuccessfully to detect hexasymmetry in the EEG signal from vowel space and did not find any (Kaya, Soltanipour and Treves, 2020), so I may be ranting off my disappointment, here. I feel, however, that this fourth hypothesis should be at least aired, for a number of reasons. One is that a hexasymmetry signal has been reported also from several other cortical areas, beyond entorhinal cortex (Constantinescu et al, 2016); true, also grid cells in rodents have been reported in other cortical areas as well (Long and Zhang, 2021; Long et al, bioRxiv, 2021), but the exact phenomenology remains to be confirmed.

Response: Thank you for the suggestion to add the hypothesis that the neural hexasymmetry observed in previous fMRI and intracranial EEG studies may be unrelated to grid cells. Following your suggestion, we have now mentioned at the end of the fourth paragraph of the Introduction that “the conjunctive grid by head-direction cell hypothesis does not necessarily depend on an alignment between the preferred head directions with the grid axes”. Furthermore, at the end of section “Potential mechanisms underlying hexadirectional population signals in the entorhinal cortex” (in the Discussion) we write: “However, none of the three hypotheses described here may be true and another mechanism may explain macroscopic grid-like representations. This includes the possibility that neural hexasymmetry is completely unrelated to grid-cell activity, previously summarized as the ‘independence hypothesis' (Kunz et al., 2019). For example, a population of head-direction cells whose preferred head directions occur at offsets of 60 degrees from each other could result in neural hexasymmetry in the absence of grid cells. The conjunctive grid by head-direction cell hypothesis thus also works without grid cells, which may explain why grid-like representations have been observed (using fMRI) in regions outside the entorhinal cortex, where rodent studies have not yet identified grid cells (Doeller et al., 2010; Constantinescu et al., 2016). In that case, however, another mechanism would be needed that could explain why the preferred head directions of different head-direction cells occur at multiples of 60 degrees. Attractor-network structures may be involved in such a mechanism, but this remains speculative at the current stage.” We now also mention the results from Long and Zhang (second paragraph of the Introduction): “Surprisingly, grid cells have also been observed in the primary somatosensory cortex in foraging rats (Long and Zhang, 2021).”

Regarding your EEG study, we have added a reference to it in the manuscript and state that it is an example for a study that did not find evidence for neural hexasymmetry (end of first paragraph of the Discussion): “We note though that some studies did not find evidence for neural hexasymmetry. For example, a surface EEG study with participants “navigating” through an abstract vowel space did not observe hexasymmetry in the EEG signal as a function of the participants’ movement direction through vowel space (Kaya et al., 2020). Another fMRI study did not find evidence for grid-like representations in the ventromedial prefrontal cortex while participants performed value-based decision making (Lee et al., 2021). This raises the question whether the detection of macroscopic grid-like representations is limited to some recording techniques (e.g., fMRI and iEEG but not surface EEG) and to what extent they are present in different tasks.”

Reviewer #1, comment #3: Second, as the authors note, the conjunctive mechanism is based on the tight coupling of a narrow head direction selectivity to one of the grid axes. They compare "ideal" with "Doeller" parameters, but to me the "Doeller" ones appear rather narrower than commonly observed and, crucially, they are applied to all cells in the simulations, whereas in reality only a proportion of cells in mEC are reported to be grid cells, only a proportion of them to be conjunctive, and only some of these to be narrowly conjunctive. Further, Gerlei et al (2020) find that conjunctive grid cells may have each of their fields modulated by different head directions, a truly surprising phenomenon that, if extensive, seems to me to cast doubts on the relation between mass activity hexasymmetry and single grid cells.

Response: We have revised the manuscript in several ways to address the different aspects of this comment.

Firstly, we agree with the reviewer that our “Doeller” parameter for the tuning width is narrower than commonly observed. We have therefore reevaluated the concentration parameter κ_c in the ‘realistic’ case from 10 rad-2 (corresponding to a tuning width of 18o) to 4 rad-2 (corresponding to a tuning width of 29o). We chose this value by referring to Supplementary Figure 3 of Doeller et al. (2010). In their figure, the tuning curves usually cover between one sixth and one third of a circle. Since stronger head-direction tuning contributes the most to the resulting hexasymmetry, we chose a value of κ_c=4 for the tuning parameter, which corresponds to a tuning width (= half width) of 29o (full width of roughly one sixth of a circle). Regarding the coupling of the preferred head directions to the grid axes, the specific value of the jitter σc = 3 degrees that quantifies the coupling of the head-direction preference to the grid axes was extracted from the 95% confidence interval given in the third row of the Table in Supplementary Figure 5b of Doeller et al. 2010. We now better explain the origin of these values in our new Methods section “Parameter estimation” and provide an overview of all parameter values in Table 1.

Furthermore, in response to your comment, we have revised Figure 2E to show neural hexasymmetries for a larger range of values of the jitter (σc from 0 to 30 degrees), going way beyond the values that Doeller et al. suggested. We have also added a new supplementary figure (Figure 2 – figure supplement 1) where we further extend the range of tuning widths (parameter κ_c) to 60 degrees. This provides the reader with a comprehensive understanding of what parameter values are needed to reach a particular hexasymmetry.

Regarding your comments on the prevalence of conjunctive grid by head-direction cells, we have revised the manuscript to make it explicit that the actual percentage of conjunctive cells with the necessary properties may be low in the entorhinal cortex (first paragraph of section “A note on our choice of the values of model parameters” of the Discussion): “Empirical studies in rodents found a wide range of tuning widths among grid cells ranging from broad to narrow (Doeller et al., 2010; Sargolini et al., 2006). The percentage of conjunctive cells in the entorhinal cortex with a sufficiently narrow tuning may thus be low. Such distributions (with a proportionally small amount of narrowly tuned conjunctive cells) lead to low values in the absolute hexasymmetry. The neural hexasymmetry in this case would be driven by the subset of cells with sufficiently narrow tuning widths. If this causes the neural hexasymmetry to drop below noise levels, the statistical evaluation of this hypothesis would change.” In addition, in Figure 5, we have applied the coupling between preferred head directions and grid axes to only one third of all grid cells (parameter pc= ⅓ in Table 1), following the values reported by Boccara et al. 2010 and Sargolini et al. 2006. To strengthen the link between Figure 5 and Figure 2, we now state the hexasymmetry when using pc= ⅓ along with a ‘realistic’ tuning width and jitter for head-direction modulated grid cells in Figure 2H. Additionally, we performed new simulations where we observed a linear relationship (above the noise floor) between the proportion of conjunctive cells and the hexasymmetry. This shall help the reader understand the effect of a reduced percentage of conjunctive cells on the absolute hexasymmetry values. We have added these results as a new supplementary figure (Figure 2 – figure supplement 2).

Finally, regarding your comment on the findings by Gerlei et al. 2020, we now reference this study in our manuscript and discuss the possible implications (second paragraph of section “A note on our choice of the values of model parameters” of the Discussion): “Additionally, while we assumed that all conjunctive grid cells maintain the same preferred head direction between different firing fields, conjunctive grid cells have also been shown to exhibit different preferred head directions in different firing fields (Gerlei et al., 2020). This could lead to hexadirectional modulation if the different preferred head directions are offset by 60o from each other, but will not give rise to hexadirectional modulation if the preferred head directions are randomly distributed. To the best of our knowledge, the distribution of preferred head directions was not quantified by Gerlei et al. (2020), thus this remains an open question.”

Reviewer #1, comment #4: Finally, a variant of the fourth hypothesis is that the hexasymmetry might be produced by a clustering of head direction preferences across head direction cells similar to that hypothesized in the first hypothesis, but without such cells having to fire in grid patterns. If head direction selectivity is so clustered, who needs the grids? This would explain why hexasymmetry is ubiquitous, and could easily be explored computationally by, in fact, a simplification of the models considered in this study.

Response: We fully agree with you. We now explain this possibility in the Introduction where we introduce the conjunctive grid by head-direction cell hypothesis (fourth paragraph of the Introduction) and return to it in the Discussion (section “Potential mechanisms underlying hexadirectional population signals in the entorhinal cortex”). There, we now also explain that in such a case another mechanism would be needed to ensure that the preferred head directions of head-direction cells exhibit six-fold rotational symmetry.

Reviewer #2 (Public Review):

Reviewer #2, comment #1: Grid cells - originally discovered in single-cell recordings from the rodent entorhinal cortex, and subsequently identified in single-cell recordings from the human brain - are believed to contribute to a range of cognitive functions including spatial navigation, long-term memory function, and inferential reasoning. Following a landmark study by Doeller et al. (Nature, 2010), a plethora of human neuroimaging studies have hypothesised that grid cell population activity might also be reflected in the six-fold (or 'hexadirectional') modulation of the BOLD signal (following the six-fold rotational symmetry exhibited by individual grid cell firing patterns), or in the amplitude of oscillatory activity recorded using MEG or intracranial EEG. The mechanism by which these network-level dynamics might arise from the firing patterns of individual grid cells remains unclear, however.

In this study, Khalid and colleagues use a combination of computational modelling and mathematical analysis to evaluate three competing hypotheses that describe how the hexadirectional modulation of population firing rates (taken as a simple proxy for the BOLD, MEG, or iEEG signal) might arise from the firing patterns of individual grid cells. They demonstrate that all three mechanisms could account for these network-level dynamics if a specific set of conditions relating to the agent's movement trajectory and the underlying properties of grid cell firing patterns are satisfied.

The computational modelling and mathematic analyses presented here are rigorous, clearly motivated, and intuitively described. In addition, these results are important both for the interpretation of hexadirectional modulation in existing data sets and for the design of future experiments and analyses that aim to probe grid cell population activity. As such, this study is likely to have a significant impact on the field by providing a firmer theoretical basis for the interpretation of neuroimaging data. To my mind, the only weakness is the relatively limited focus on the known properties of grid cells in rodent entorhinal cortex, and the network level activity that these firing patterns might be expected to produce under each hypothesis. Strengthening the link with existing neurobiology would further enhance the importance of these results for those hoping to assay grid cell firing patterns in recordings of ensemble-level neural activity.

Response: Thank you very much for reviewing our manuscript and your positive assessment. Following your comments, we have revised the manuscript to more closely link our simulations to known properties of grid cells in the rodent entorhinal cortex.

Reviewer #3 (Public Review):

Reviewer #3, comment #1: This is an interesting and carefully carried out theoretical analysis of potential explanations for hexadirectional modulation of neural population activity that has been reported in the human entorhinal cortex and some other cortical regions. The previously reported hexadirectional modulation is of considerable interest as it has been proposed to be a proxy for the activation of grid cell networks. However, the extent to which this proposal is consistent with the known firing properties of grids hasn't received the attention it perhaps deserves. By comparing the predictions of three different models this study imposes constraints on possible mechanisms and generates predictions that can be tested through future experimentation.

Overall, while the conclusions of the study are convincing, I think the usefulness to the field would be increased if null hypotheses were more carefully considered and if the authors' new metric for hexadirectional modulation (H) could be directly contrasted with previously used metrics. For example, if the effect sizes for hexadirectional modulation in the previous fMRI and EEG data could be more directly compared with those of the models here, then this could help in establishing the extent to which the experimental hexadirectional modulation stands out from path hexasymmetry and how close it comes to the striking modulation observed with the conjunctive models. It could also be helpful to consider scenarios in which hexadirectional modulation is independent of grid firing, for example perhaps with appropriate coordination of head direction cell firing.

Response: Thanks for reviewing our manuscript and for the overall positive assessment. The new Methods section “Implementation of previously used metrics” starts with the following sentences: “We applied three previously used metrics to our framework: the Generalized Linear Model (GLM) method by Doeller et al. 2010; the GLM method with binning by Kunz et al. 2015; and the circular-linear correlation method by Maidenbaum et al. 2018.” We have created a new supplementary figure (Figure 5 – figure supplement 4) in which we compare the results from these other methods to the results of our new method. Overall, the results are highly similar, indicating that all these methods are equally suited to test for a hexadirectional modulation of neural activity.

In section “Implementation of previously used metrics” we then explain: “In brief, in the GLM method (e.g. used in Doeller et al., 2010), the hexasymmetry is found in two steps: the orientation of the hexadirectional modulation is first estimated on the first half of the data by using the regressors and on the time-discrete fMRI activity (Equation 9), with θt being the movement direction of the subject in time step t. The amplitude of the signal is then estimated on the second half of the data using the single regressor , where . The hexasymmetry is then evaluated as .

The GLM method with binning (e.g. used in Kunz et al., 2015) uses the same procedure as the GLM method for estimating the grid orientation in the first half of the data, but the amplitude is estimated differently on the second half by a regressor that has a value 1 if θt is aligned with a peak of the hexadirectional modulation (aligned if , modulo operator) and a value of -1 if θt is misaligned. The hexasymmetry is then calculated from the amplitude in the same way as in the GLM method.

The circular-linear correlation method (e.g. used in Maidenbaum et al., 2018) is similar to the GLM method in that it uses the regressors β1 cos(6θ_t) and β2 on the time-discrete mean activity, but instead of using β1 and β2 to estimate the orientation of the hexadirectional modulation, the beta values are directly used to estimate the hexasymmetry using the relation .”

For each of the three previously used metrics and our new method, we estimated the resulting hexasymmetry (new Figure 5 – figure supplement 4 in the manuscript). In the Methods section “Implementation of previously used metrics” we then continue with our explanations: “Regarding the statistical evaluation, each method evaluates the size of the neural hexasymmetry differently. Specifically, the new method developed in our manuscript compares the neural hexasymmetry to path hexasymmetry to test whether neural hexasymmetry is significantly above path hexasymmetry. For the two generalized linear model (GLM) methods, we compare the hexasymmetry to zero (using the Mann-Whitney U test) to establish significance. Hexasymmetry values can be negative in these approaches, allowing the statistical comparison against 0. Negative values occur when the estimated grid orientation from the first data half does not match the grid orientation from the second data half. Regarding the statistical evaluation of the circular-linear correlation method, we calculated a z-score by comparing each empirical observation of the hexasymmetry to hexasymmetries from a set of surrogate distributions (as in Maidenbaum et al., 2018). We then calculate a p-value by comparing the distribution of z-scores versus zero using a Mann-Whitney U test. We use the z-scores instead of the hexasymmetry for the circular-linear correlation method to match the procedure used in Maidenbaum et al. (2018). We obtained the surrogate distributions by circularly shifting the vector of movement directions relative to the time dependent vector of firing rates. For random walks, the vector is shifted by a random number drawn from a uniform distribution defined with the same length as the number of time points in the vector of movement directions. For the star-like walks and piecewise linear walks, the shift is a random integer multiplied by the number of time points in a linear segment. Circularly shifting the vector of movement directions scrambles the correlations between movement direction and neural activity while preserving their temporal structure.”

The results of these simulations, i.e. the comparison of our new method to previously used metrics, are summarized in Figure 5 – figure supplement 4 and show qualitatively identical findings when using the different methods. We have added this information also to the manuscript in the third paragraph of section “Quantification of hexasymmetry of neural activity and trajectories” of the Methods: “Empirical (fMRI/iEEG) studies (e.g. Doeller et al., 2010; Kunz et al., 2015; Maidenbaum et al., 2018) addressed this problem of trajectories spuriously contributing to hexasymmetry by fitting a Generalized Linear Model (GLM) to the time discrete fMRI/iEEG activity. In contrast, our new approach to hexasymmetry in Equation (12) quantifies the contribution of the path to the neural hexasymmetry explicitly, and has the advantage that it allows an analytical treatment (see next section). Comparing our new method with previous methods for evaluating hexasymmetry led to qualitatively identical statistical effects (Figure 5 – figure supplement 4).” We have also added a pointer to this new supplementary figure in the caption of Figure 5 in the manuscript: “For a comparison between our method and previously used methods for evaluating hexasymmetry, see Figure 5 – figure supplement 4.”

Author Response

Reviewer #1 (Public Review):

This manuscript will interest cognitive scientists, neuroimaging researchers, and neuroscientists interested in the systems-level organization of brain activity. The authors describe four brain states that are present across a wide range of cognitive tasks and determine that the relative distribution of the brain states shows both commonalities and differences across task conditions.

The authors characterized the low-dimensional latent space that has been shown to capture the major features of intrinsic brain activity using four states obtained with a Hidden Markov Model. They related the four states to previously-described functional gradients in the brain and examined the relative contribution of each state under different cognitive conditions. They showed that states related to the measured behavior for each condition differed, but that a common state appears to reflect disengagement across conditions. The authors bring together a state-of-the-art analysis of systemslevel brain dynamics and cognitive neuroscience, bridging a gap that has long needed to be bridged.

The strongest aspect of the study is its rigor. The authors use appropriate null models and examine multiple datasets (not used in the original analysis) to demonstrate that their findings replicate. Their thorough analysis convincingly supports their assertion that common states are present across a variety of conditions, but that different states may predict behavioural measures for different conditions. However, the authors could have better situated their work within the existing literature. It is not that a more exhaustive literature review is needed-it is that some of their results are unsurprising given the work reported in other manuscripts; some of their work reinforces or is reinforced by prior studies; and some of their work is not compared to similar findings obtained with other analysis approaches. While space is not unlimited, some of these gaps are important enough that they are worth addressing:

We appreciate the reviewer’s thorough read of our manuscript and positive comments on its rigor and implications. We agree that the original version of the manuscript insufficiently situated this work in the existing literature. We have made extensive revisions to better place our findings in the context of prior work. These changes are described in detail below.

1) The authors' own prior work on functional connectivity signatures of attention is not discussed in comparison to the latest work. Neither is work from other groups showing signatures of arousal that change over time, particularly in resting state scans. Attention and arousal are not the same things, but they are intertwined, and both have been linked to large-scale changes in brain activity that should be captured in the HMM latent states. The authors should discuss how the current work fits with existing studies.

Thank you for raising this point. We agree that the relationship between low-dimensional latent states and predefined activity and functional connectivity signatures is an important and interesting question in both attention research and more general contexts. Here, we did not empirically relate the brain states examined in this study and functional connectivity signatures previously investigated in our lab (e.g., Rosenberg et al., 2016; Song et al., 2021a) because the research question and methodological complexities deserved separate attention that go beyond the scope of this paper. Therefore, we conceptually addressed the reviewer’s question on how functional connectivity signatures of attention are related to the brain states that were observed here. Next, we asked how arousal relates to the brain states by indirectly predicting arousal levels of each brain state based on its activity patterns’ spatial resemblance to the predefined arousal network template (Goodale et al., 2021).

Latent states and dynamic functional connectivity

Previous work suggested that, on medium time scales (~20-60 seconds), changes in functional connectivity signatures of sustained attention (Rosenberg et al., 2020) and narrative engagement (Song et al., 2021a) predicted changes in attentional states. How do these attention-related functional connectivity dynamics relate to latent state dynamics, measured on a shorter time scale (1 second)?

Theoretically, there are reasons to think that these measures are related but not redundant. Both HMM and dynamic functional connectivity provide summary measures of the whole-brain functional interactions that evolve over time. Whereas HMM identifies recurring low-dimensional brain states, dynamic functional connectivity used in our and others’ prior studies captures high-dimensional dynamical patterns. Furthermore, while the mixture Gaussian function utilized to infer emission probability in our HMM infers the states from both the BOLD activity patterns and their interactions, functional connectivity considers only pairwise interactions between regions of interests. Thus, with a theoretical ground that the brain states can be characterized at multiple scales and different methods (Greene et al., 2023), we can hypothesize that the both measures could (and perhaps, should be able to) capture brain-wide latent state changes. For example, if we were to apply kmeans clustering methods on the sliding window-based dynamic functional connectivity as in Allen et al. (2014), the resulting clusters could arguably be similar to the latent states derived from the HMM.

However, there are practical reasons why the correspondence between our prior dynamic functional connectivity models and current HMM states is difficult to test directly. A time point-bytime point matching of the HMM state sequence and dynamic functional connectivity is not feasible because, in our prior work, dynamic functional connectivity was measured in a sliding time window (~20-60 seconds), whereas the HMM state identification is conducted at every TR (1 second). An alternative would be to concatenate all time points that were categorized as each HMM state to compute representative functional connectivity of that state. This “splicing and concatenating” method, however, disrupts continuous BOLD-signal time series and has not previously been validated for use with our dynamic connectome-based predictive models. In addition, the difference in time series lengths across states would make comparisons of the four states’ functional connectomes unfair.

One main focus of our manuscript was to relate brain dynamics (HMM state dynamics) to static manifold (functional connectivity gradients). We agree that a direct link between two measures of brain dynamics, HMM and dynamic functional connectivity, is an important research question. However, due to some intricacies that needed to be addressed to answer this question, we felt that it was beyond the scope of our paper. We are eager, however, to explore these comparisons in future work which can more thoroughly address the caveats associated with comparing models of sustained attention, narrative engagement, and arousal defined using different input features and methods.

Arousal, attention, and latent neural state dynamics

Next, the reviewer posed an important question about the relationship between arousal, attention, and latent states. The current study was designed to assess the relationship between attention and latent state dynamics. However, previous neuroimaging work showed that low-dimensional brain dynamics reflect fluctuations in arousal (Raut et al., 2021; Shine et al., 2016; Zhang et al., 2023). Behavioral studies showed that attention and arousal hold a non-linear relationship, for example, mind-wandering states are associated with lower arousal and externally distracted states are associated with higher arousal, when both these states indicate low attention (Esterman and Rothlein, 2019; Unsworth and Robison, 2018, 2016).

To address the reviewer’s suggestion, we wanted to test if our brain states reflected changes in arousal, but we did not collect relevant behavioral or physiological measures. Therefore, to indirectly test for relationships, we predicted levels of arousal in brain states by applying the “arousal network template” defined by Dr. Catie Chang’s group (Chang et al., 2016; Falahpour et al., 2018; Goodale et al., 2021). The arousal network template was created from resting-state fMRI data to predict arousal levels indicated by eye monitoring and electrophysiological signals. In the original study, the arousal level at each time point was predicted by the correlation between the BOLD activity patterns of each TR to the arousal template. The more similar the whole-brain activation pattern was to the arousal network template, the higher the participant was predicted to be aroused at that moment. This activity pattern-based model was generalized to fMRI data during tasks (Goodale et al., 2021).

We correlated the arousal template to the activity patterns of the four brain states that were inferred by the HMM. The DMN state was positively correlated with the arousal template (r=0.264) and the SM state was negatively correlated with the arousal template (r=-0.303) (Author response image 1). These values were not tested for significance because they were single observations. While speculative, this may suggest that participants are in a high arousal state during the DMN state and a low arousal state during the SM state. Together with our results relating brain states to attention, it is possible that the SM state is a common state indicating low arousal and low attention. On the other hand, the DMN state, a signature of a highly aroused state, may benefit gradCPT task performance but not necessarily in engaging with a sitcom episode. However, because this was a single observation and we did not collect a physiological measure of arousal to validate this indirect prediction result, we did not include the result in the manuscript. We hope to more directly test this question in future work with behavioral and physiological measures of arousal.

Author response image 1.

Changes made to the manuscript

Importantly, we agree with the reviewer that a theoretical discussion about the relationships between functional connectivity, latent states, gradients, as well as attention and arousal was a critical omission from the original Discussion. We edited the Discussion to highlight past literature on these topics and encourage future work to investigate these relationships.

[Manuscript, page 11] “Previous studies showed that large-scale neural dynamics that evolve over tens of seconds capture meaningful variance in arousal (Raut et al., 2021; Zhang et al., 2023) and attentional states (Rosenberg et al., 2020; Yamashita et al., 2021). We asked whether latent neural state dynamics reflect ongoing changes in attention in both task and naturalistic contexts.”

[Manuscript, page 17] “Previous work showed that time-resolved whole-brain functional connectivity (i.e., paired interactions of more than a hundred parcels) predicts changes in attention during task performance (Rosenberg et al., 2020) as well as movie-watching and story-listening (Song et al., 2021a). Future work could investigate whether functional connectivity and the HMM capture the same underlying “brain states” to bridge the results from the two literatures. Furthermore, though the current study provided evidence of neural state dynamics reflecting attention, the same neural states may, in part, reflect fluctuations in arousal (Chang et al., 2016; Zhang et al., 2023). Complementing behavioral studies that demonstrated a nonlinear relationship between attention and arousal (Esterman and Rothlein, 2019; Unsworth and Robison, 2018, 2016), future studies collecting behavioral and physiological measures of arousal can assess the extent to which attention explains neural state dynamics beyond what can be explained by arousal fluctuations.”

2) The 'base state' has been described in a number of prior papers (for one early example, see https://pubmed.ncbi.nlm.nih.gov/27008543). The idea that it might serve as a hub or intermediary for other states has been raised in other studies, and discussion of the similarity or differences between those studies and this one would provide better context for the interpretation of the current work. One of the intriguing findings of the current study is that the incidence of this base state increases during sitcom watching, the strongest evidence to date is that it has a cognitive role and is not merely a configuration of activity that the brain must pass through when making a transition.

We greatly appreciate the reviewer’s suggestion of prior papers. We were not aware of previous findings of the base state at the time of writing the manuscript, so it was reassuring to see consistent findings. In the Discussion, we highlighted the findings of Chen et al. (2016) and Saggar et al. (2022). Both studies highlighted the role of the base state as a “hub”-like transition state. However, as the reviewer noted, these studies did not address the functional relevance of this state to cognitive states because both were based on resting-state fMRI.

In our revised Discussion, we write that our work replicates previous findings of the base state that consistently acted as a transitional hub state in macroscopic brain dynamics. We also note that our study expands this line of work by characterizing what functional roles the base state plays in multiple contexts: The base state indicated high attentional engagement and exhibited the highest occurrence proportion as well as longest dwell times during naturalistic movie watching. The base state’s functional involvement was comparatively minor during controlled tasks.

[Manuscript, page 17-18] “Past resting-state fMRI studies have reported the existence of the base state. Chen et al. (2016) used the HMM to detect a state that had “less apparent activation or deactivation patterns in known networks compared with other states”. This state had the highest occurrence probability among the inferred latent states, was consistently detected by the model, and was most likely to transition to and from other states, all of which mirror our findings here. The authors interpret this state as an “intermediate transient state that appears when the brain is switching between other more reproducible brain states”. The observation of the base state was not confined to studies using HMMs. Saggar et al. (2022) used topological data analysis to represent a low-dimensional manifold of resting-state whole-brain dynamics as a graph, where each node corresponds to brain activity patterns of a cluster of time points. Topologically focal “hub” nodes were represented uniformly by all functional networks, meaning that no characteristic activation above or below the mean was detected, similar to what we observe with the base state. The transition probability from other states to the hub state was the highest, demonstrating its role as a putative transition state.

However, the functional relevance of the base state to human cognition had not been explored previously. We propose that the base state, a transitional hub (Figure 2B) positioned at the center of the gradient subspace (Figure 1D), functions as a state of natural equilibrium. Transitioning to the DMN, DAN, or SM states reflects incursion away from natural equilibrium (Deco et al., 2017; Gu et al., 2015), as the brain enters a functionally modular state. Notably, the base state indicated high attentional engagement (Figure 5E and F) and exhibited the highest occurrence proportion (Figure 3B) as well as the longest dwell times (Figure 3—figure supplement 1) during naturalistic movie watching, whereas its functional involvement was comparatively minor during controlled tasks. This significant relevance to behavior verifies that the base state cannot simply be a byproduct of the model. We speculate that susceptibility to both external and internal information is maximized in the base state—allowing for roughly equal weighting of both sides so that they can be integrated to form a coherent representation of the world—at the expense of the stability of a certain functional network (Cocchi et al., 2017; Fagerholm et al., 2015). When processing rich narratives, particularly when a person is fully immersed without having to exert cognitive effort, a less modular state with high degrees of freedom to reach other states may be more likely to be involved. The role of the base state should be further investigated in future studies.”

3) The link between latent states and functional connectivity gradients should be considered in the context of prior work showing that the spatiotemporal patterns of intrinsic activity that account for most of the structure in resting state fMRI also sweep across functional connectivity gradients (https://pubmed.ncbi.nlm.nih.gov/33549755/). In fact, the spatiotemporal dynamics may give rise to the functional connectivity gradients (https://pubmed.ncbi.nlm.nih.gov/35902649/). HMM states bear a marked resemblance to the high-activity phases of these patterns and are likely to be closely linked to them. The spatiotemporal patterns are typically obtained during rest, but they have been reported during task performance (https://pubmed.ncbi.nlm.nih.gov/30753928/) which further suggests a link to the current work. Similar patterns have been observed in anesthetized animals, which also reinforces the conclusion of the current work that the states are fundamental aspects of the brain's functional organization.

We appreciate the comments that relate spatiotemporal patterns, functional connectivity gradients, and the latent states derived from the HMM. Our work was also inspired by the papers that the reviewer suggested, especially Bolt et al.’s (2022), which compared the results of numerous dimensionality and clustering algorithms and suggested three spatiotemporal patterns that seemed to be commonly supported across algorithms. We originally cited these studies throughout the manuscript, but did not discuss them comprehensively. We have revised the Discussion to situate our findings on past work that used resting-state fMRI to study low-dimensional latent brain states.

[Manuscript, page 15-16] “This perspective is supported by previous work that has used different methods to capture recurring low-dimensional states from spontaneous fMRI activity during rest. For example, to extract time-averaged latent states, early resting-state analyses identified task-positive and tasknegative networks using seed-based correlation (Fox et al., 2005). Dimensionality reduction algorithms such as independent component analysis (Smith et al., 2009) extracted latent components that explain the largest variance in fMRI time series. Other lines of work used timeresolved analyses to capture latent state dynamics. For example, variants of clustering algorithms, such as co-activation patterns (Liu et al., 2018; Liu and Duyn, 2013), k-means clustering (Allen et al., 2014), and HMM (Baker et al., 2014; Chen et al., 2016; Vidaurre et al., 2018, 2017), characterized fMRI time series as recurrences of and transitions between a small number of states. Time-lag analysis was used to identify quasiperiodic spatiotemporal patterns of propagating brain activity (Abbas et al., 2019; Yousefi and Keilholz, 2021). A recent study extensively compared these different algorithms and showed that they all report qualitatively similar latent states or components when applied to fMRI data (Bolt et al., 2022). While these studies used different algorithms to probe data-specific brain states, this work and ours report common latent axes that follow a long-standing theory of large-scale human functional systems (Mesulam, 1998). Neural dynamics span principal axes that dissociate unimodal to transmodal and sensory to motor information processing systems.”

Reviewer #2 (Public Review):

In this study, Song and colleagues applied a Hidden Markov Model to whole-brain fMRI data from the unique SONG dataset and a grad-CPT task, and in doing so observed robust transitions between lowdimensional states that they then attributed to specific psychological features extracted from the different tasks.

The methods used appeared to be sound and robust to parameter choices. Whenever choices were made regarding specific parameters, the authors demonstrated that their approach was robust to different values, and also replicated their main findings on a separate dataset.

I was mildly concerned that similarities in some of the algorithms used may have rendered some of the inter-measure results as somewhat inevitable (a hypothesis that could be tested using appropriate null models).

This work is quite integrative, linking together a number of previous studies into a framework that allows for interesting follow-up questions.

Overall, I found the work to be robust, interesting, and integrative, with a wide-ranging citation list and exciting implications for future work.

We appreciate the reviewer’s comments on the study’s robustness and future implications. Our work was highly motivated by the reviewer’s prior work.

Reviewer #3 (Public Review):

My general assessment of the paper is that the analyses done after they find the model are exemplary and show some interesting results. However, the method they use to find the number of states (Calinski-Harabasz score instead of log-likelihood), the model they use generally (HMM), and the fact that they don't show how they find the number of states on HCP, with the Schaeffer atlas, and do not report their R^2 on a test set is a little concerning. I don't think this perse impedes their results, but it is something that they can improve. They argue that the states they find align with long-standing ideas about the functional organization of the brain and align with other research, but they can improve their selection for their model.

We appreciate the reviewer’s thorough read of the paper, evaluation of our analyses linking brain states to behavior as “exemplary”, and important questions about the modeling approach. We have included detailed responses below and updated the manuscript accordingly.

Strengths:

• Use multiple datasets, multiple ROIs, and multiple analyses to validate their results

• Figures are convincing in the sense that patterns clearly synchronize between participants

• Authors select the number of states using the optimal model fit (although this turns out to be a little more questionable due to what they quantify as 'optimal model fit')

We address this concern on page 30-31 of this response letter.

• Replication with Schaeffer atlas makes results more convincing

• The analyses around the fact that the base state acts as a flexible hub are well done and well explained

• Their comparison of synchrony is well-done and comparing it to resting-state, which does not have any significant synchrony among participants is obvious, but still good to compare against.

• Their results with respect to similar narrative engagement being correlated with similar neural state dynamics are well done and interesting.

• Their results on event boundaries are compelling and well done. However, I do not find their Chang et al. results convincing (Figure 4B), it could just be because it is a different medium that explains differences in DMN response, but to me, it seems like these are just altogether different patterns that can not 100% be explained by their method/results.

We entirely agree with the reviewer that the Chang et al. (2021) data are different in many ways from our own SONG dataset. Whereas data from Chang et al. (2021) were collected while participants listened to an audio-only narrative, participants in the SONG sample watched and listened to audiovisual stimuli. They were scanned at different universities in different countries with different protocols by different research groups for different purposes. That is, there are numerous reasons why we would expect the model should not generalize. Thus, we found it compelling and surprising that, despite all of these differences between the datasets, the model trained on the SONG dataset generalized to the data from Chang et al. (2021). The results highlighted a robust increase in the DMN state occurrence and a decrease in the base state occurrence after the narrative event boundaries, irrespective of whether the stimulus was an audiovisual sitcom episode or a narrated story. This external model validation was a way that we tested the robustness of our own model and the relationship between neural state dynamics and cognitive dynamics.

• Their results that when there is no event, transition into the DMN state comes from the base state is 50% is interesting and a strong result. However, it is unclear if this is just for the sitcom or also for Chang et al.'s data.

We apologize for the lack of clarity. We show the statistical results of the two sitcom episodes as well as Chang et al.’s (2021) data in Figure 4—figure supplement 2 in our original manuscript. Here, we provide the exact values of the base-to-DMN state transition probability, and how they differ across moments after event boundaries compared to non-event boundaries.

For sitcom episode 1, the probability of base-to-DMN state transition was 44.6 ± 18.8 % at event boundaries whereas 62.0 ± 10.4 % at non-event boundaries (FDR-p = 0.0013). For sitcom episode 2, the probability of base-to-DMN state transition was 44.1 ± 18.0 % at event boundaries whereas 62.2 ± 7.6 % at non-event boundaries (FDR-p = 0.0006). For the Chang et al. (2021) dataset, the probability of base-to-DMN state transition was 33.3 ± 15.9 % at event boundaries whereas 58.1 ± 6.4 % at non-event boundaries (FDR-p < 0.0001). Thus, our result, “At non-event boundaries, the DMN state was most likely to transition from the base state, accounting for more than 50% of the transitions to the DMN state” (pg 11, line 24-25), holds true for both the internal and external datasets.

• The involvement of the base state as being highly engaged during the comedy sitcom and the movie are interesting results that warrant further study into the base state theory they pose in this work.

• It is good that they make sure SM states are not just because of head motion (P 12).

• Their comparison between functional gradient and neural states is good, and their results are generally well-supported, intuitive, and interesting enough to warrant further research into them. Their findings on the context-specificity of their DMN and DAN state are interesting and relate well to the antagonistic relationship in resting-state data.

Weaknesses:

• Authors should train the model on part of the data and validate on another

Thank you for raising this issue. To the best of our knowledge, past work that applied the HMM to the fMRI data has conducted training and inference on the same data, including initial work that implemented HMM on the resting-state fMRI (Baker et al., 2014; Chen et al., 2016; Vidaurre et al., 2018, 2017) as well as more recent work that applied HMMs to the task or movie-watching fMRI (Cornblath et al., 2020; Taghia et al., 2018; van der Meer et al., 2020; Yamashita et al., 2021). That is, the parameters—emission probability, transition probability, and initial probability—were estimated from the entire dataset and the latent state sequence was inferred using the Viterbi algorithm on the same dataset.

However, we were also aware of the potential problem this may have. Therefore, in our recent work asking a different research question in another fMRI dataset (Song et al., 2021b), we trained an HMM on a subset of the dataset (moments when participants were watching movie clips in the original temporal order) and inferred latent state sequence of the fMRI time series in another subset of the dataset (moments when participants were watching movie clips in a scrambled temporal order). To the best of our knowledge, this was the first paper that used different segments of the data to fit and infer states from the HMM.

In the current study, we wanted to capture brain states that underlie brain activity across contexts. Thus, we presented the same-dataset training and inference procedure as our primary result. However, for every main result, we also showed results where we separated the data used for model fitting and state inference. That is, we fit the HMM on the SONG dataset, primarily report the inference results on the SONG dataset, but also report inference on the external datasets that were not included in model fitting. The datasets used were the Human Connectome Project dataset (Van Essen et al., 2013), Chang et al. (2021) audio-listening dataset, Rosenberg et al. (2016) gradCPT dataset, and Chen et al. (2017) Sherlock dataset.

However, to further address the concern of the reviewer whether the HMM fit is reliable when applied to held-out data, we computed the reliability of the HMM inference by conducting crossvalidations and split-half reliability analysis.

(1) Cross-validation

To separate the dataset used for HMM training and inference, we conducted cross-validation on the SONG dataset (N=27) by training the model with the data from 26 participants and inferring the latent state sequence of the held-out participant.

First, we compared the robustness of the model training by comparing the mean activity patterns of the four latent states fitted at the group level (N=27) with the mean activity patterns of the four states fitted across cross-validation folds. Pearson’s correlations between the group-level vs. cross-validated latent states’ mean activity patterns were r = 0.991 ± 0.010, with a range from 0.963 to 0.999.

Second, we compared the robustness of model inference by comparing the latent state sequences that were inferred at the group level vs. from held-out participants in a cross-validation scheme. All fMRI conditions had mean similarity higher than 90%; Rest 1: 92.74 ± 5.02 %, Rest2: 92.74 ± 4.83 %, GradCPT face: 92.97 ± 6.41 %, GradCPT scene: 93.27 ± 5.76 %, Sitcom ep1: 93.31 ± 3.92 %, Sitcom ep2: 93.13 ± 4.36 %, Documentary: 92.42 ± 4.72 %.

Third, with the latent state sequences inferred from cross-validation, we replicated the analysis of Figure 3 to test for synchrony of the latent state sequences across participants. The crossvalidated results were highly similar to manuscript Figure 3, which was generated from the grouplevel analysis. Mean synchrony of latent state sequences are as follows: Rest 1: 25.90 ± 3.81%, Rest 2: 25.75 ± 4.19 %, GradCPT face: 27.17 ± 3.86 %, GradCPT scene: 28.11 ± 3.89 %, Sitcom ep1: 40.69 ± 3.86%, Sitcom ep2: 40.53 ± 3.13%, Documentary: 30.13 ± 3.41%.

Author response image 2.

(2) Split-half reliability

To test for the internal robustness of the model, we randomly assigned SONG dataset participants into two groups and conducted HMM separately in each. Similarity (Pearson’s correlation) between the two groups’ activation patterns were DMN: 0.791, DAN: 0.838, SM: 0.944, base: 0.837. The similarity of the covariance patterns were DMN: 0.995, DAN: 0.996, SM: 0.994, base: 0.996.

Author response image 3.

We further validated the split-half reliability of the model using the HCP dataset, which contains data of a larger sample (N=119). Similarity (Pearson’s correlation) between the two groups’ activation patterns were DMN: 0.998, DAN: 0.997, SM: 0.993, base: 0.923. The similarity of the covariance patterns were DMN: 0.995, DAN: 0.996, SM: 0.994, base: 0.996.

Together the cross-validation and split-half reliability results demonstrate that the HMM results reported in the manuscript are reliable and robust to the way we conducted the analysis. The result of the split-half reliability analysis is added in the Results.

[Manuscript, page 3-4] “Neural state inference was robust to the choice of 𝐾 (Figure 1—figure supplement 1) and the fMRI preprocessing pipeline (Figure 1—figure supplement 5) and consistent when conducted on two groups of randomly split-half participants (Pearson’s correlations between the two groups’ latent state activation patterns: DMN: 0.791, DAN: 0.838, SM: 0.944, base: 0.837).”

• Comparison with just PCA/functional gradients is weak in establishing whether HMMs are good models of the timeseries. Especially given that the HMM does not explain a lot of variance in the signal (~0.5 R^2 for only 27 brain regions) for PCA. I think they don't report their own R^2 of the timeseries

We agree with the reviewer that the PCA that we conducted to compare with the explained variance of the functional gradients was not directly comparable because PCA and gradients utilize different algorithms to reduce dimensionality. To make more meaningful comparisons, we removed the data-specific PCA results and replaced them with data-specific functional gradients (derived from the SONG dataset). This allows us to directly compare SONG-specific functional gradients with predefined gradients (derived from the resting-state HCP dataset from Margulies et al. [2016]). We found that the degrees to which the first two predefined gradients explained whole-brain fMRI time series (SONG: 𝑟! = 0.097, HCP: 0.084) were comparable to the amount of variance explained by the first two data-specific gradients (SONG: 𝑟! = 0.100, HCP: 0.086). Thus, the predefined gradients explain as much variance in the SONG data time series as SONG-specific gradients do. This supports our argument that the low-dimensional manifold is largely shared across contexts, and that the common HMM latent states may tile the predefined gradients.

These analyses and results were added to the Results, Methods, and Figure 1—figure supplement 8. Here, we only attach changes to the Results section for simplicity, but please see the revised manuscript for further changes.

[Manuscript, page 5-6] “We hypothesized that the spatial gradients reported by Margulies et al. (2016) act as a lowdimensional manifold over which large-scale dynamics operate (Bolt et al., 2022; Brown et al., 2021; Karapanagiotidis et al., 2020; Turnbull et al., 2020), such that traversals within this manifold explain large variance in neural dynamics and, consequently, cognition and behavior (Figure 1C). To test this idea, we situated the mean activity values of the four latent states along the gradients defined by Margulies et al. (2016) (see Methods). The brain states tiled the two-dimensional gradient space with the base state at the center (Figure 1D; Figure1—figure supplement 7). The Euclidean distances between these four states were maximized in the two-dimensional gradient space, compared to a chance where the four states were inferred from circular-shifted time series (p < 0.001). For the SONG dataset, the DMN and SM states fell at more extreme positions of the primary gradient than expected by chance (both FDR-p values = 0.004; DAN and SM states, FDRp values = 0.171). For the HCP dataset, the DMN and DAN states fell at more extreme positions on the primary gradient (both FDR-p values = 0.004; SM and base states, FDR-p values = 0.076). No state was consistently found at the extremes of the secondary gradient (all FDR-p values > 0.021).

We asked whether the predefined gradients explain as much variance in neural dynamics as latent subspace optimized for the SONG dataset. To do so, we applied the same nonlinear dimensionality reduction algorithm to the SONG dataset’s ROI time series. Of note, the SONG dataset includes 18.95% rest, 15.07% task, and 65.98% movie-watching data whereas the data used by Margulies et al. (2016) was 100% rest. Despite these differences, the SONG-specific gradients closely resembled the predefined gradients, with significant Pearson’s correlations observed for the first (r = 0.876) and second (r = 0.877) gradient embeddings (Figure 1—figure supplement 8). Gradients identified with the HCP data also recapitulated Margulies et al.’s (2016) first (r = 0.880) and second (r = 0.871) gradients. We restricted our analysis to the first two gradients because the two gradients together explained roughly 50% of the entire variance of functional brain connectome (SONG: 46.94%, HCP: 52.08%), and the explained variance dropped drastically from the third gradients (more than 1/3 drop compared to second gradients). The degrees to which the first two predefined gradients explained whole-brain fMRI time series (SONG: 𝑟! = 0.097, HCP: 0.084) were comparable to the amount of variance explained by the first two data-specific gradients (SONG: 𝑟! = 0.100, HCP: 0.086; Figure 1—figure supplement 8). Thus, the low-dimensional manifold captured by Margulies et al. (2016) gradients is highly replicable, explaining brain activity dynamics as well as data-specific gradients, and is largely shared across contexts and datasets. This suggests that the state space of whole-brain dynamics closely recapitulates low-dimensional gradients of the static functional brain connectome.”

The reviewer also pointed out that the PCA-gradient comparison was weak in establishing whether HMMs are good models of the time series. However, we would like to point out that the purpose of the comparison was not to validate the performance of the HMM. Instead, we wanted to test whether the gradients introduced by Margulies et al. (2016) could act as a generalizable lowdimensional manifold of brain state dynamics. To argue that the predefined gradients are a shared manifold, these gradients should explain SONG data fMRI time series as much as the principal components derived directly from the SONG data. Our results showed comparable 𝑟!, both in predefined gradient vs. data-specific PC comparisons and predefined gradient vs. data-specific gradient comparisons, which supported our argument that the predefined gradients could be the shared embedding space across contexts and datasets.

The reviewer pointed out that the 𝑟2 of ~0.5 is not explaining enough variance in the fMRI signal. However, we respectfully disagree with this point because there is no established criterion for what constitutes a high or low 𝑟2 for this type of analysis. Of note, previous literature that also applied PCA to fMRI time series (Author response image 4A and 4B) (Lynn et al., 2021; Shine et al., 2019) also found that the cumulative explained variance of top 5 principal components is around 50%. Author response image 4C shows cumulative variances to which gradients explain the functional connectome of the resting-state fMRI data (Margulies et al., 2016).

Author response image 4.

Finally, the reviewer pointed out that the 𝑟! of the HMM-derived latent sequence to the fMRI time series should be reported. However, there is no standardized way of measuring the explained variance of the HMM inference. There is no report of explained variance in the traditional HMMfMRI papers (Baker et al., 2014; Chen et al., 2016; Vidaurre et al., 2018, 2017). Rather than 𝑟!, the HMM computes the log likelihood of the model fit. However, because log likelihood values are dependent on the number of data points, studies do not report log likelihood values nor do they use these metrics to interpret the goodness of model fit.

To ask whether the goodness of the HMM fit was significant above chance, we compared the log likelihood of the HMM to the log likelihood distribution of the null HMM fits. First, we extracted the log likelihood of the HMM fit with the real fMRI time series. We iterated this 1,000 times when calculating null HMMs using the circular-shifted fMRI time series. The log likelihood of the real model was significantly higher than the chance distribution, with a z-value of 2182.5 (p < 0.001). This indicates that the HMM explained a large variance in our fMRI time series data, significantly above chance.

• Authors do not specify whether they also did cross-validation for the HCP dataset to find 4 clusters

We apologize for the lack of clarity. When we computed the Calinski-Harabasz score with the HCP dataset, three was chosen as the most optimal number of states (Author response image 5A). When we set K as 3, the HMM inferred the DMN, DAN, and SM states (Author response image 5C). The base state was included when K was set to 4 (Author response image 5B). The activation pattern similarities of the DMN, DAN, and SM states were r = 0.981, 0.984, 0.911 respectively.

Author response image 5.

We did not use K = 3 for the HCP data replication because we were not trying to test whether these four states would be the optimal set of states in every dataset. Although the CalinskiHarabasz score chose K = 3 because it showed the best clustering performance, this does not mean that the base state is not meaningful to this dataset. Likewise, the latent states that are inferred when we increase/decrease the number of states are also meaningful states. For example, in Figure 1—figure supplement 1, we show an example of the SONG dataset’s latent states when we set K to 7. The seven latent states included the DAN, SM, and base states, the DMN state was subdivided into DMN-A and DMN-B states, and the FPN state and DMN+VIS state were included. Setting a higher number of states like K = 7 would mean that we are capturing brain state dynamics in a higher dimension than when using K = 4. Because we are utilizing a higher number of states, a model set to K = 7 would inevitably capture a larger variance of fMRI time series than a model set to K = 4.

The purpose of latent state replication with the HCP dataset was to validate the generalizability of the DMN, DAN, SM, and base states. Before characterizing these latent states’ relevance to cognition, we needed to verify that these latent states were not simply overfit to the SONG dataset. The fact that the HMM revealed a similar set of latent states when applied to the HCP dataset suggested that the states were not merely specific to SONG data.

To make our points clearer in the manuscript, we emphasized that we are not arguing for the four states to be the exclusive states. We made edits to Discussion as follows.

[Manuscript, page 16] “Our study adopted the assumption of low dimensionality of large-scale neural systems, which led us to intentionally identify only a small number of states underlying whole-brain dynamics. Importantly, however, we do not claim that the four states will be the optimal set of states in every dataset and participant population. Instead, latent states and patterns of state occurrence may vary as a function of individuals and tasks (Figure 1—figure supplement 2). Likewise, while the lowest dimensions of the manifold (i.e., the first two gradients) were largely shared across datasets tested here, we do not argue that it will always be identical. If individuals and tasks deviate significantly from what was tested here, the manifold may also differ along with changes in latent states (Samara et al., 2023). Brain systems operate at different dimensionalities and spatiotemporal scales (Greene et al., 2023), which may have different consequences for cognition. Asking how brain states and manifolds—probed at different dimensionalities and scales—flexibly reconfigure (or not) with changes in contexts and mental states is an important research question for understanding complex human cognition.”

• One of their main contributions is the base state but the correlation between the base state in their Song dataset and the HCP dataset is only 0.399

This is a good point. However, there is precedent for lower spatial pattern correlation of the base state compared to other states in the literature.

Compared to the DMN, DAN, and SM states, the base state did not show characteristic activation or deactivation of functional networks. Most of the functional networks showed activity levels close to the mean (z = 0). With this flattened activation pattern, relatively low activation pattern similarity was observed between the SONG base state and the HCP base state.

In Figure 1—figure supplement 6, we write, “The DMN, DAN, and SM states showed similar mean activity patterns. We refrained from making interpretations about the base state’s activity patterns because the mean activity of most of the parcels was close to z = 0”.

A similar finding has been reported in a previous work by Chen et al. (2016) that discovered the base state with HMM. State 9 (S9) of their results is comparable to our base state. They report that even though the spatial correlation coefficient of the brain state from the split-half reliability analysis was the lowest for S9 due to its low degrees of activation or deactivation, S9 was stably inferred by the HMM. The following is a direct quote from their paper:

“To the best of our knowledge, a state similar to S9 has not been presented in previous literature. We hypothesize that S9 is the “ground” state of the brain, in which brain activity (or deactivity) is similar for the entire cortex (no apparent activation or deactivation as shown in Fig. 4). Note that different groups of subjects have different spatial patterns for state S9 (Fig. 3A). Therefore, S9 has the lowest reproducible spatial pattern (Fig. 3B). However, its temporal characteristics allowed us to distinguish it consistently from other states.” (Chen et al., 2016)

Thus, we believe our data and prior results support the existence of the “base state”.

• Figure 1B: Parcellation is quite big but there seems to be a gradient within regions

This is a function of the visualization software. Mean activity (z) is the same for all voxels within a parcel. To visualize the 3D contours of the brain, we chose an option in the nilearn python function that smooths the mean activity values based on the surface reconstructed anatomy.

In the original manuscript, our Methods write, “The brain surfaces were visualized with nilearn.plotting.plot_surf_stat_map. The parcel boundaries in Figure 1B are smoothed from the volume-to-surface reconstruction.”

• Figure 1D: Why are the DMNs further apart between SONG and HCP than the other states

To address this question, we first tested whether the position of the DMN states in the gradient space is significantly different for the SONG and HCP datasets. We generated surrogate HMM states from the circular-shifted fMRI time series and positioned the four latent states and the null DMN states in the 2-dimensional gradient space (Author response image 6).

Author response image 6.

We next tested whether the Euclidean distance between the SONG dataset’s DMN state and the HCP dataset’s DMN state is larger than would be expected by chance (Author response image 7). To do so, we took the difference between the DMN state positions and compared it to the 1,000 differences generated from the surrogate latent states. The DMN states of the SONG and HCP datasets did not significantly differ in the Gradient 1 dimension (two-tailed test, p = 0.794). However, as the reviewer noted, the positions differed significantly in the Gradient 2 dimension (p = 0.047). The DMN state leaned more towards the Visual gradient in the SONG dataset, whereas it leaned more towards the Somatosensory-Motor gradient in the HCP dataset.

Author response image 7.

Though we cannot claim an exact reason for this across-dataset difference, we note a distinctive difference between the SONG and HCP datasets. Both datasets largely included resting-state, controlled tasks, and movie watching. The SONG dataset included 18.95% of rest, 15.07% of task, and 65.98% of movie watching. The task only contained the gradCPT, i.e., sustained attention task. On the other hand, the HCP dataset included 52.71% of rest, 24.35% of task, and 22.94% of movie watching. There were 7 different tasks included in the HCP dataset. It is possible that different proportions of rest, task, and movie watching, and different cognitive demands involved with each dataset may have created data-specific latent states.

• Page 5 paragraph starting at L25: Their hypothesis that functional gradients explain large variance in neural dynamics needs to be explained more, is non-trivial especially because their R^2 scores are so low (Fig 1. Supplement 8) for PCA

We address this concern on page 21-23 of this response letter.

• Generally, I do not find the PCA analysis convincing and believe they should also compare to something like ICA or a different model of dynamics. They do not explain their reasoning behind assuming an HMM, which is an extremely simplified idea of brain dynamics meaning they only change based on the previous state.

We appreciate this perspective. We replaced the Margulies et al.’s (2016) gradient vs. SONGspecific PCA comparison with a more direct Margulies et al.’s (2016) gradient vs. SONG-specific gradient comparison as described on page 21-23 of this response letter.

More broadly, we elected to use HMM because of recent work showing correspondence between low-dimensional HMM states and behavior (Cornblath et al., 2020; Taghia et al., 2018; van der Meer et al., 2020; Yamashita et al., 2021). We also found the model’s assumption—a mixture Gaussian emission probability and first-order Markovian transition probability—to be the most suited to analyzing the fMRI time series data. We do not intend to claim that other data-reduction techniques would not also capture low-dimensional, behaviorally relevant changes in brain activity. Instead, our primary focus was identifying a set of latent states that generalize (i.e., recur) across multiple contexts and understanding how those states reflect cognitive and attentional states.

Although a comparison of possible data-reduction algorithms is out of the scope of the current work, an exhaustive comparison of different models can be found in Bolt et al. (2022). The authors compared dozens of latent brain state algorithms spanning zero-lag analysis (e.g., principal component analysis, principal component analysis with Varimax rotation, Laplacian eigenmaps, spatial independent component analysis, temporal independent component analysis, hidden Markov model, seed-based correlation analysis, and co-activation patterns) to time-lag analysis (e.g., quasi-periodic pattern and lag projections). Bolt et al. (2022) writes “a range of empirical phenomena, including functional connectivity gradients, the task-positive/task-negative anticorrelation pattern, the global signal, time-lag propagation patterns, the quasiperiodic pattern and the functional connectome network structure, are manifestations of the three spatiotemporal patterns.” That is, many previous findings that used different methods essentially describe the same recurring latent states. A similar argument was made in previous papers (Brown et al., 2021; Karapanagiotidis et al., 2020; Turnbull et al., 2020).

We agree that the HMM is a simplified idea of brain dynamics. We do not argue that the four number of states can fully explain the complexity and flexibility of cognition. Instead, we hoped to show that there are different dimensionalities to which the brain systems can operate, and they may have different consequences to cognition. We “simplified” neural dynamics to a discrete sequence of a small number of states. However, what is fascinating is that these overly “simplified” brain state dynamics can explain certain cognitive and attentional dynamics, such as event segmentation and sustained attention fluctuations. We highlight this point in the Discussion.

[Manuscript, page 16] “Our study adopted the assumption of low dimensionality of large-scale neural systems, which led us to intentionally identify only a small number of states underlying whole-brain dynamics. Importantly, however, we do not claim that the four states will be the optimal set of states in every dataset and participant population. Instead, latent states and patterns of state occurrence may vary as a function of individuals and tasks (Figure 1—figure supplement 2). Likewise, while the lowest dimensions of the manifold (i.e., the first two gradients) were largely shared across datasets tested here, we do not argue that it will always be identical. If individuals and tasks deviate significantly from what was tested here, the manifold may also differ along with changes in latent states (Samara et al., 2023). Brain systems operate at different dimensionalities and spatiotemporal scales (Greene et al., 2023), which may have different consequences for cognition. Asking how brain states and manifolds—probed at different dimensionalities and scales—flexibly reconfigure (or not) with changes in contexts and mental states is an important research question for understanding complex human cognition.”

• For the 25- ROI replication it seems like they again do not try multiple K values for the number of states to validate that 4 states are in fact the correct number.

In the manuscript, we do not argue that the four will be the optimal number of states in any dataset. (We actually predict that this may differ depending on the amount of data, participant population, tasks, etc.) Instead, we claim that the four identified in the SONG dataset are not specific (i.e., overfit) to that sample, but rather recur in independent datasets as well. More broadly we argue that the complexity and flexibility of human cognition stem from the fact that computation occurs at multiple dimensions and that the low-dimensional states observed here are robustly related to cognitive and attentional states. To prevent misunderstanding of our results, we emphasized in the Discussion that we are not arguing for a fixed number of states. A paragraph included in our response to the previous comment (page 16 in the manuscript) illustrates this point.

• Fig 2B: Colorbar goes from -0.05 to 0.05 but values are up to 0.87

We apologize for the confusion. The current version of the figure is correct. The figure legend states, “The values indicate transition probabilities, such that values in each row sums to 1. The colors indicate differences from the mean of the null distribution where the HMMs were conducted on the circular-shifted time series.”

We recognize that this complicates the interpretation of the figure. However, after much consideration, we decided that it was valuable to show both the actual transition probabilities (values) and their difference from the mean of null HMMs (colors). The values demonstrate the Markovian property of latent state dynamics, with a high probability of remaining in the same state at consecutive moments and a low probability of transitioning to a different state. The colors indicate that the base state is a transitional hub state by illustrating that the DMN, DAN, and SM states are more likely to transition to the base state than would be expected by chance.

• P 16 L4 near-critical, authors need to be more specific in their terminology here especially since they talk about dynamic systems, where near-criticality has a specific definition. It is unclear which definition they are looking for here.

We agree that our explanation was vague. Because we do not have evidence for this speculative proposal, we removed the mention of near-criticality. Instead, we focus on our observation as the base state being the transitional hub state within a metastable system.

[Manuscript, page 17-18] “However, the functional relevance of the base state to human cognition had not been explored previously. We propose that the base state, a transitional hub (Figure 2B) positioned at the center of the gradient subspace (Figure 1D), functions as a state of natural equilibrium. Transitioning to the DMN, DAN, or SM states reflects incursion away from natural equilibrium (Deco et al., 2017; Gu et al., 2015), as the brain enters a functionally modular state. Notably, the base state indicated high attentional engagement (Figure 5E and F) and exhibited the highest occurrence proportion (Figure 3B) as well as the longest dwell times (Figure 3—figure supplement 1) during naturalistic movie watching, whereas its functional involvement was comparatively minor during controlled tasks. This significant relevance to behavior verifies that the base state cannot simply be a byproduct of the model. We speculate that susceptibility to both external and internal information is maximized in the base state—allowing for roughly equal weighting of both sides so that they can be integrated to form a coherent representation of the world—at the expense of the stability of a certain functional network (Cocchi et al., 2017; Fagerholm et al., 2015). When processing rich narratives, particularly when a person is fully immersed without having to exert cognitive effort, a less modular state with high degrees of freedom to reach other states may be more likely to be involved. The role of the base state should be further investigated in future studies.”

• P16 L13-L17 unnecessary

We prefer to have the last paragraph as a summary of the implications of this paper. However, if the length of this paper becomes a problem as we work towards publication with the editors, we are happy to remove these lines.

• I think this paper is solid, but my main issue is with using an HMM, never explaining why, not showing inference results on test data, not reporting an R^2 score for it, and not comparing it to other models. Secondly, they use the Calinski-Harabasz score to determine the number of states, but not the log-likelihood of the fit. This clearly creates a bias in what types of states you will find, namely states that are far away from each other, which likely also leads to the functional gradient and PCA results they have. Where they specifically talk about how their states are far away from each other in the functional gradient space and correlated to (orthogonal) components. It is completely unclear to me why they used this measure because it also seems to be one of many scores you could use with respect to clustering (with potentially different results), and even odd in the presence of a loglikelihood fit to the data and with the model they use (which does not perform clustering).

(1) Showing inference results on test data

We address this concern on page 19-21 of this response letter.

(2) Not reporting 𝑹𝟐 score

We address this concern on page 21-23 of this response letter.

(3) Not comparing the HMM model to other models

We address this concern on page 27-28 of this response letter.

(4) The use of the Calinski-Harabasz score to determine the number of states rather than the log-likelihood of the model fit

To our knowledge, the log-likelihood of the model fit is not used in the HMM literature. It is because the log-likelihood tends to increase monotonically as the number of states increases. Baker et al. (2014) illustrates this problem, writing:

“In theory, it should be possible to pick the optimal number of states by selecting the model with the greatest (negative) free energy. In practice however, we observe that the free energy increases monotonically up to K = 15 states, suggesting that the Bayes-optimal model may require an even higher number of states.”

Similarly, the following figure is the log-likelihood estimated from the SONG dataset. Similar to the findings of Baker et al. (2014), the log-likelihood monotonically increased as the number of states increased (Author response image 8, right). The measures like AIC or BIC, which account for the number of parameters, also have the same issue of monotonic increase.

Author response image 8.

Because there is “no straightforward data-driven approach to model order selection” (Baker et al., 2014), past work has used different approaches to decide on the number of states. For example, Vidaurre et al. (2018) iterated over a range of the number of states to repeat the same HMM training and inference procedures 5 times using the same hyperparameters. They selected the number of states that showed the highest consistency across iterations. Gao et al. (2021) tested the clustering performance of the model output using the Calinski-Harabasz score. The number of states that showed the highest within-cluster cohesion compared to the across-cluster separation was selected as the number of states. Chang et al. (2021) applied HMM to voxels of the ventromedial prefrontal cortex using a similar clustering algorithm, writing: “To determine the number of states for the HMM estimation procedure, we identified the number of states that maximized the average within-state spatial similarity relative to the average between-state similarity”. In our previous paper (Song et al., 2021b), we reported both the reliability and clustering performance measures to decide on the number of states.

In the current manuscript, the model consistency criterion from Vidaurre et al. (2018) was ineffective because the HMM inference was extremely robust (i.e., always inferring the exact same sequence) due to a large number of data points. Thus, we used the Calinski-Harabasz score as our criterion for the number of states selected.

We agree with the reviewer that the selection of the number of states is critical to any study that implements HMM. However, the field lacks a consensus on how to decide on the number of states in the HMM, and the Calinski-Harabasz score has been validated in previous studies. Most importantly, the latent states’ relationships with behavioral and cognitive measures give strong evidence that the latent states are indeed meaningful states. Again, we are not arguing that the optimal set of states in any dataset will be four nor are we arguing that these four states will always be the optimal states. Instead, the manuscript proposes that a small number of latent states explains meaningful variance in cognitive dynamics.

• Grammatical error: P24 L29 rendering seems to have gone wrong

Our intention was correct here. To avoid confusion, we changed “(number of participantsC2 iterations)” to “(#𝐶!iterations, where N=number of participants)” (page 26 in the manuscript).

Questions:

• Comment on subject differences, it seems like they potentially found group dynamics based on stimuli, but interesting to see individual differences in large-scale dynamics, and do they believe the states they find mostly explain global linear dynamics?

We agree with the reviewer that whether low-dimensional latent state dynamics explain individual differences—above and beyond what could be explained by the high-dimensional, temporally static neural signatures of individuals (e.g., Finn et al., 2015)—is an important research question. However, because the SONG dataset was collected in a single lab, with a focus on covering diverse contexts (rest, task, and movie watching) over 2 sessions, we were only able to collect 27 participants. Due to this small sample size, we focused on investigating group-level, shared temporal dynamics and across-condition differences, rather than on investigating individual differences.

Past work has studied individual differences (e.g., behavioral traits like well-being, intelligence, and personality) using the HMM (Vidaurre et al., 2017). In the lab, we are working on a project that investigates latent state dynamics in relation to individual differences in clinical symptoms using the Healthy Brain Network dataset (Ji et al., 2022, presented at SfN; Alexander et al., 2017).

Finally, the reviewer raises an interesting question about whether the latent state sequence that was derived here mostly explains global linear dynamics as opposed to nonlinear dynamics. We have two responses: one methodological and one theoretical. First, methodologically, we defined the emission probabilities as a linear mixture of Gaussian distributions for each input dimension with the state-specific mean (mean fMRI activity patterns of the networks) and variance (functional covariance across networks). Therefore, states are modeled with an assumption of linearity of feature combinations. Theoretically, recent work supports in favor of nonlinearity of large-scale neural dynamics, especially as tasks get richer and more complex (Cunningham and Yu, 2014; Gao et al., 2021). However, whether low-dimensional latent states should be modeled nonlinearly—that is, whether linear algorithms are insufficient at capturing latent states compared to nonlinear algorithms—is still unknown. We agree with the reviewer that the assumption of linearity is an interesting topic in systems neuroscience. However, together with prior work which showed how numerous algorithms—either linear or nonlinear—recapitulated a common set of latent states, we argue that the HMM provides a strong low-dimensional model of large-scale neural activity and interaction.

• P19 L40 why did the authors interpolate incorrect or no-responses for the gradCPT runs? It seems more logical to correct their results for these responses or to throw them out since interpolation can induce huge biases in these cases because the data is likely not missing at completely random.

Interpolating the RTs of the trials without responses (omission errors and incorrect trials) is a standardized protocol for analyzing gradCPT data (Esterman et al., 2013; Fortenbaugh et al., 2018, 2015; Jayakumar et al., 2023; Rosenberg et al., 2013; Terashima et al., 2021; Yamashita et al., 2021). The choice of this analysis is due to an assumption that sustained attention is a continuous attentional state; the RT, a proxy for the attentional state in the gradCPT literature, is a noisy measure of a smoothed, continuous attentional state. Thus, the RTs of the trials without responses are interpolated and the RT time courses are smoothed by convolving with a gaussian kernel.

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Author Response

Reviewer #2 (Public Review):

"The cellular architecture of memory modules in Drosophila supports stochastic input integration" is a classical biophysical compartmental modelling study. It takes advantage of some simple current injection protocols in a massively complex mushroom body neuron called MBON-a3 and compartmental models that simulate the electrophysiological behaviour given a detailed description of the anatomical extent of its neurites.

This work is interesting in a number of ways:

• The input structure information comes from EM data (Kenyon cells) although this is not discussed much in the paper - The paper predicts a potentially novel normalization of the throughput of KC inputs at the level of the proximal dendrite and soma - It claims a new computational principle in dendrites, this didn’t become very clear to me Problems I see:

• The current injections did not last long enough to reach steady state (e.g. Figure 1FG), and the model current injection traces have two time constants but the data only one (Figure 2DF). This does not make me very confident in the results and conclusions.

These are two important but separate questions that we would like to address in turn.

As for the first, in our new recordings using cytoplasmic GFP to identify MBON-alpha3, we performed both a 200 ms current injection and performed prolonged recordings of 400 ms to reach steady state (for all 4 new cells 1’-4’). For comparison with the original dataset we mainly present the raw traces for 200 ms recordings in Figure 1 Supplement 2. In addition, we now provide a direct comparison of these recordings (200 ms versus 400 ms) and did not observe significant differences in tau between these data (Figure 1 Supplement 2 K). This comparison illustrates that the 200 ms current injection reaches a maximum voltage deflection that is close to the steady state level of the prolonged protocol. Importantly, the critical parameter (tau) did not change between these datasets.

Regarding the second question, the two different time constants, we thank the reviewer for pointing this out. Indeed, while the simulated voltage follows an approximately exponential decay which is, by design, essentially identical to the measured value (τ≈ 16ms, from Table 1; ee Figure 1 Supplement 2 for details), the voltage decays and rises much faster immediately following the onset and offset of the current injections. We believe that this is due to the morphology of this neuron. Current injection, and voltage recordings, are at the soma which is connected to the remainder of the neuron by a long and thin neurite. This ’remainder’ is, of course, in linear size, volume and surface (membrane) area much larger than the soma, see Fig 2A. As a result, a current injection will first quickly charge up the membrane of the soma, resulting in the initial fast voltage changes seen in Fig 2D,F, before the membrane in the remainder of the cell is charged, with the cell’s time constant τ.

We confirmed this intuition by running various simplified simulations in Neuron which indeed show a much more rapid change at step changes in injected current than over the long-term. Indeed, we found that the pattern even appears in the simplest possible two-compartment version of the neuron’s equivalent circuit which we solved in an all-purpose numerical simulator of electrical circuitry (https://www.falstad.com/circuit). The circuit is shown in Figure 1. We chose rather generic values for the circuit components, with the constraints that the cell capacitance, chosen as 15pF, and membrane resistance, chosen as 1GΩ, are in the range of the observed data (as is, consequently, its time constant which is 15ms with these choices); see Table 1 of the manuscript. We chose the capacitance of the soma as 1.5pF, making the time constant of the soma (1.5ms) an order of magnitude shorter than that of the cell.

Figure 1: Simplified circuit of a small soma (left parallel RC circuit) and the much larger remainder of a cell (right parallel RC circuit) connected by a neurite (right 100MΩ resistor). A current source (far left) injects constant current into the soma through the left 100MΩ resistor.

Figure 2 shows the somatic voltage in this circuit (i.e., at the upper terminal of the 1.5pF capacitor) while a -10pA current is injected for about 4.5ms, after which the current is set back to zero. The combination of initial rapid change, followed by a gradual change with a time constant of ≈ 15ms is visible at both onset and offset of the current injection. Figure 3 show the voltage traces plotted for a duration of approximately one time constant, and Fig 4 shows the detailed shape right after current onset.

Figure 2: Somatic voltage in the circuit in Fig. 1 with current injection for about 4.5ms, followed by zero current injection for another ≈ 3.5ms.

Figure 3: Somatic voltage in the circuit, as in Fig. 2 but with current injected for approx. 15msvvvvv

While we did not try to quantitatively assess the deviation from a single-exponential shape of the voltage in Fig. 2E, a more rapid increase at the onset and offset of the current injection is clearly visible in this Figure. This deviation from a single exponential is smaller than what we see in the simulation (both in Fig 2D of the manuscript, and in the results of the simplified circuit here in the rebuttal). We believe that the effect is smaller in Fig. E because it shows the average over many traces. It is much more visible in the ’raw’ (not averaged) traces. Two randomly selected traces from the first of the recorded neurons are shown in Figure 2 Supplement 2 C. While the non-averaged traces are plagued by artifacts and noise, the rapid voltage changes are visible essentially at all onsets and offsets of the current injection.

Figure 4: Somatic voltage in the circuit, as in Fig. 2 but showing only for the time right after current onset, about 2.3ms.

We have added a short discussion of this at the end of Section 2.3 to briefly point out this observation and its explanation. We there also refer to the simplified circuit simulation and comparison with raw voltage traces which is now shown in the new Figure 2 Supplement 2.

• The time constant in Table 1 is much shorter than in Figure 1FG?

No, these values are in agreement. To facilitate the comparison we now include a graphical measurement of tau from our traces in Figure 1 Supplement 2 J.

• Related to this, the capacitance values are very low maybe this can be explained by the model’s wrong assumption of tau?

Indeed, the measured time constants are somewhat lower than what might be expected. We believe that this is because after a step change of the injected current, an initial rapid voltage change occurs in the soma, where the recordings are taken. The measured time constant is a combination of the ’actual’ time constant of the cell and the ’somatic’ (very short) time constant of the soma. Please see our explanations above.

Importantly, the value for tau from Table 1 is not used explicitly in the model as the parameters used in our simulation are determined by optimal fits of the simulated voltage curves to experimentally obtained data.

• That latter in turn could be because of either space clamp issues in this hugely complex cell or bad model predictions due to incomplete reconstructions, bad match between morphology and electrophysiology (both are from different datasets?), or unknown ion channels that produce non-linear behaviour during the current injections.

Please see our detailed discussion above. Furthermore, we now provide additional recordings using cytoplasmic GFP as a marker for the identification of MBON-alpha3 and confirm our findings. We agree that space-clamp issues could interfere with our recordings in such a complex cell. However, our approach using electrophysiological data should still be superior to any other approach (picking text book values). As we injected negative currents for our analysis at least voltage-gated ion channels should not influence our recordings.

• The PRAXIS method in NEURON seems too ad hoc. Passive properties of a neuron should probably rather be explored in parameter scans.

We are a bit at a loss of what is meant by the PRAXIS method being "too ad hoc." The PRAXIS method is essentially a conjugate gradient optimization algorithm (since no explicit derivatives are available, it makes the assumption that the objective function is quadratic). This seems to us a systematic way of doing a parameter scan, and the procedure has been used in other related models, e.g. the cited Gouwens & Wilson (2009) study.

Questions I have:

• Computational aspects were previously addressed by e.g. Larry Abbott and Gilles Laurent (sparse coding), how do the findings here distinguish themselves from this work

In contrast to the work by Abbott and Laurent that addressed the principal relevance and suitability of sparse and random coding for the encoding of sensory information in decision making, here we address the cellular and computational mechanisms that an individual node (KC>MBON) play within the circuitry. As we use functional and morphological relevant data this study builds upon the prior work but significantly extends the general models to a specific case. We think this is essential for the further exploration of the topic.

• What is valence information?

Valence information is the information whether a stimulus is good (positive valence, e.g. sugar in appetitive memory paradigms, or negative valence in aversive olfactory conditioning - the electric shock). Valence information is provided by the dopaminergic system. Dopaminergic neurons are in direct contact with the KC>MBON circuitry and modify its synaptic connectivity when olfactory information is paired with a positive or negative stimulus.

• It seems that Martin Nawrot’s work would be relevant to this work

We are aware of the work by the Nawrot group that provided important insights into the processing of information within the olfactory mushroom body circuitry. We now highlight some of his work. His recent work will certainly be relevant for our future studies when we try to extend our work from an individual cell to networks.

• Compactification and democratization could be related to other work like Otopalik et al 2017 eLife but also passive normalization. The equal efficiency in line 427 reminds me of dendritic/synaptic democracy and dendritic constancy

Many thanks for pointing this out. This is in line with the comments from reviewer 1 and we now highlight these papers in the relevant paragraph in the discussion (line 442ff).

• The morphology does not obviously seem compact, how unusual would it be that such a complex dendrite is so compact?

We should have been more careful in our terminology, making clear that when we write ’compact’ we always mean ’electrotonically compact," in the sense that the physical dimensions of the neuron are small compared to its characteristic electrotonic length (usually called λ). The degree of a dendritic structure being electrotonically compact is determined by the interaction of morphology, size and conductances (across the membrane and along the neurites). We don’t believe that one of these factors alone (e.g. morphology) is sufficient to characterize the electrical properties of a dendritic tree. We have now clarified this in the relevant section.

• What were the advantages of using the EM circuit?

The purpose of our study is to provide a "realistic" model of a KC>MBON node within the memory circuitry. We started our simulations with random synaptic locations but wondered whether such a stochastic model is correct, or whether taking into account the detailed locations and numbers of synaptic connections of individual KCs would make a difference to the computation. Therefore we repeated the simulations using the EM data. We now address the point between random vs realistic synaptic connectivity in Figure 4F. We do not observe a significant difference but this may become more relevant in future studies if we compute the interplay between MBONs activated by overlapping sets of KCs. We simply think that utilizing the EM data gets us one step closer to realistic models.

• Isn’t Fig 4E rather trivial if the cell is compact?

We believe this figure is a visually striking illustration that shows how electrotonically compact the cell is. Such a finding may be trivial in retrospect, once the data is visualized, but we believe it provides a very intuitive description of the cell behavior.

Overall, I am worried that the passive modelling study of the MBON-a3 does not provide enough evidence to explain the electrophysiological behaviour of the cell and to make accurate predictions of the cell’s responses to a variety of stochastic KC inputs.

In our view our model adequately describes the behavior of the MBON with the most minimal (passive) model. Our approach tries to make the least assumptions about the electrophysiological properties of the cell. We think that based on the current knowledge our approach is the best possible approach as thus far no active components within the dendritic or axonal compartments of Drosophila MBONs have been described. As such, our model describes the current status which explains the behavior of the cell very well. We aim to refine this model in the future if experimental evidence requires such adaptations.

Reviewer #3 (Public Review):

This manuscript presents an analysis of the cellular integration properties of a specific mushroom body output neuron, MBON-α3, using a combination of patch clamp recordings and data from electron microscopy. The study demonstrates that the neuron is electrotonically compact permitting linear integration of synaptic input from Kenyon cells that represent odor identity.

Strengths of the manuscript:

The study integrates morphological data about MBON-α3 along with parameters derived from electrophysiological measurements to build a detailed model. 2) The modeling provides support for existing models of how olfactory memory is related to integration at the MBON.

Weaknesses of the manuscript:

The study does not provide experimental validation of the results of the computational model.

The goal of our study is to use computational approaches to provide insights into the computation of the MBON as part of the olfactory memory circuitry. Our data is in agreement with the current model of the circuitry. Our study therefore forms the basis for future experimental studies; those would however go beyond the scope of the current work.

The conclusion of the modeling analysis is that the neuron integrates synaptic inputs almost completely linearly. All the subsequent analyses are straightforward consequences of this result.

We do, indeed, find that synaptic integration in this neuron is almost completely linear. We demonstrate that this result holds in a variety of different ways. All analyses in the study serve this purpose. These results are in line with the findings by Hige and Turner (2013) who demonstrated that also synaptic integration at PN>KC synapses is highly linear. As such our data points to a feature conservation to the next node of this circuit.

The manuscript does not provide much explanation or intuition as to why this linear conclusion holds.

We respectfully disagree. We demonstrate that this linear integration is a combination of the size of the cell and the combination of its biophysical parameters, mainly the conductances across and along the neurites. As to why it holds, our main argument is that results based on the linear model agree with all known (to us) empirical results, and this is the simplest model.

In general, there is a clear takeaway here, which is that the dendritic tree of MBON-α3 in the lobes is highly electrotonically compact. The authors did not provide much explanation as to why this is, and the paper would benefit from a clearer conclusion. Furthermore, I found the results of Figures 4 and 5 rather straightforward given this previous observation. I am sceptical about whether the tiny variations in, e.g. Figs. 3I and 5F-H, are meaningful biologically.

Please see the comment above as to the ’why’ we believe the neuron is electrotonically compact: a model with this assumption agrees well with empirically found results.

We agree that the small variations in Fig 5F-H are likely not biologically meaningful. We state this now more clearly in the figure legends and in the text. This result is important to show, however. It is precisely because these variations are small, compared to the differences between voltage differences between different numbers of activated KCs (Fig 5D) or different levels of activated synapses (Fig 5E) that we can conclude that a 25% change in either synaptic strength or number can represent clearly distinguishable internal states, and that both changes have the same effect. It is important to show these data, to allow the reader to compare the differences that DO matter (Fig 5D,E) and those that DON’T (Fig 5F-H).

The same applies to Fig 3I. The reviewer is entirely correct: the differences in the somatic voltage shown in Figure 3I are minuscule, less than a micro-Volt, and it is very unlikely that these difference have any biological meaning. The point of this figure is exactly to show this!. It is to demonstrate quantitatively the transformation of the large differences between voltages in the dendritic tree and the nearly complete uniform voltage at the soma. We feel that this shows very clearly the extreme "democratization" of the synaptic input!

Author Response

Reviewer #1 (Public Review):

Nicotine preference is highly variable between individuals. The paper by Mondoloni et al. provided some insight into the potential link between IPN nAchR heterogeneity with male nicotine preference behavior. They scored mice using the amount of nicotine consumption, as well as the rats' preference of the drug using a two-bottle choice experiment. An interesting heterogeneity in nicotine-drinking profiles was observed in adult male mice, with about half of the mice ceasing nicotine consumption at high concentrations. They observed a negative association of nicotine intake with nicotine-evoked currents in the antiparticle nucleus (IPN). They also identified beta4-containing nicotine acetylcholine receptors, which exhibit an association with nicotine aversion. The behavioral differentiation of av vs. n-avs and identification of IPN variability, both in behavioral and electrophysiological aspects, add an important candidate for analyzing individual behavior in addiction.

The native existence of beta4-nAchR heterogeneity is an important premise that supports the molecules to be the candidate substrate of variabilities. However, only knockout and re-expression models were used, which is insufficient to mimic the physiological state that leads to variability in nicotine preference.

We’d like to thank reviewer 1 for his/her positive remarks and for suggesting important control experiments. Regarding the reviewer’s latest comment on the link between b4 and variability, we would like to point out that the experiment in which mice were put under chronic nicotine can be seen as another way to manipulate the physiological state of the animal. Indeed, we found that chronic nicotine downregulates b4 nAChR expression levels (but has no effect on residual nAChR currents in b4-/- mice) and reduces nicotine aversion. Therefore, these results also point toward a role of IPN b4 nAChRs in nicotine aversion. We have now performed additional experiments and analyses to address these concerns and to reinforce our demonstration.

Reviewer #2 (Public Review):

In the current study, Mondoloni and colleagues investigate the neural correlates contributing to nicotine aversion and its alteration following chronic nicotine exposure. The question asked is important to the field of individual vulnerability to drug addiction and has translational significance. First, the authors identify individual nicotine consumption profiles across isogenic mice. Further, they employed in vivo and ex vivo physiological approaches to defining how antiparticle nuclei (IPn) neuronal response to nicotine is associated with nicotine avoidance. Additionally, the authors determine that chronic nicotine exposure impairs IPn neuronal normal response to nicotine, thus contributing to higher amounts of nicotine consumption. Finally, they used transgenic and viralmediated gene expression approaches to establish a causal link between b4 nicotine receptor function and nicotine avoidance processes.

The manuscript and experimental strategy are well designed and executed; the current dataset requires supplemental analyses and details to exclude possible alternatives. Overall, the results are exciting and provide helpful information to the field of drug addiction research, individual vulnerability to drug addiction, and neuronal physiology. Below are some comments aiming to help the authors improve this interesting study.

We would like to thank the reviewer for his/her positive remarks and we hope the new version of the manuscript will clarify his/her concerns.

1) The authors used a two-bottle choice behavioral paradigm to investigate the neurophysiological substrate contributing to nicotine avoidance behaviors. While the data set supporting the author's interpretation is compelling and the experiments are well-conducted, a few supplemental control analyses will strengthen the current manuscript.

a) The bitter taste of nicotine might generate confounds in the data interpretation: are the mice avoiding the bitterness or the nicotine-induced physiological effect? To address this question, the authors mixed nicotine with saccharine, thus covering the bitterness of nicotine. Additionally, the authors show that all the mice exposed to quinine avoid it, and in comparison, the N-Av don't avoid the bitterness of the nicotine-saccharine solution. Yet it is unclear if Av and N-Av have different taste discrimination capacities and if such taste discrimination capacities drive the N-Av to consume less nicotine. Would Av and N-Av mice avoid quinine differently after the 20-day nicotine paradigm? Would the authors observe individual nicotine drinking behaviors if nicotine/quinine vs. quinine were offered to the mice?

As requested by all three reviewers, we have now performed a two-bottle choice experiment to verify whether different sensitivities to the bitterness of the nicotine solution could explain the different sensitivities to the aversive properties of nicotine. Indeed, even though we used saccharine to mask the bitterness of the nicotine solution, we cannot fully exclude the possibility that the taste capacity of the mice could affect their nicotine consumption. Reviewers 1 and 2 suggested to perform nicotine/quinine versus quinine preference tests, but we were afraid that forcing mice to drink an aversive, quinine-containing solution might affect the total volume of liquid consumed per day, and also might create a “generalized conditioned aversion to drinking water - detrimental to overall health and a confounding factor” as pointed out by reviewer 3. Therefore, we designed the experiment a little differently.

In this two-bottle choice experiment, mice were first proposed a high concentration of nicotine (100 µg/ml) which has previously been shown to induce avoidance behavior in mice (Figure 3C). Then, mice were offered three increasing concentrations of quinine: 30, 100 and 300 µM. Quinine avoidance was dose dependent, as expected: it was moderate for 30 µM but almost absolute for 300 µM quinine. We then investigated whether nicotine and quinine avoidances were linked. We found no correlation between nicotine and quinine preference (new Figure: Figure 1- supplementary figure 1D). This new experiment strongly suggests that aversion to the drug is not directly tied to the sensitivity of mice to the bitter taste of nicotine.

Other results reinforce this conclusion. First, none of the b4-/- mice (0/13) showed aversion to nicotine, whereas about half of the virally-rescued animals (8/17, b4 re-expressed in the IPN of b4-/- mice) showed nicotine aversion, a proportion similar to the one observed in WT mice. This experiment makes a clear, direct link between the expression of b4 nAChRs in the IPN and aversion to the drug.

Furthermore, we also verified that the sensitivity of b4-/- mice to bitterness is not different from that of WT mice (new Figure 4 – figure supplement 1B). This new result indicates that the reason why b4-/- mice consume more nicotine than WT mice is not because they have a reduced sensitivity bitterness.

Together, these new experiments strongly suggests that interindividual differences in sensitivity to the bitterness of nicotine play little role in nicotine consumption behavior in mice.

b) Metabolic variabilities amongst isogenic mice have been observed. Thus, while the mice consume different amounts of nicotine, changes in metabolic processes, thus blood nicotine concentrations, could explain differences in nicotine consumption and neurophysiology across individuals. The authors should control if the blood concentration of nicotine metabolites between N-Av and Av are similar when consuming identical amounts of nicotine (50ug/ml), different amounts (200ug/ml), and in response to an acute injection of a fixed nicotine quantity.

We agree with the reviewer that metabolic variabilities could explain (at least in part) the differences observed between avoiders and non-avoiders. But other factors could also play a role, such as stress level (there is a strong interaction between stress and nicotine addiction, as shown by our group (PMID: 29155800, PMID: 30361503) and others), hierarchical ranking, epigenetic factors etc… Our goal in this study is not to examine all possible sources of variability. What is striking about our results is that deletion of a single gene (encoding the nAChR b4 subunit) is sufficient to eliminate nicotine avoidance, and that re-expression of this receptor subunit in the IPN is sufficient to restore nicotine avoidance. In addition, we observe a strong correlation between the amplitude of nicotineinduced current in the IPN, and nicotine consumption. Therefore, the expression level of b4 in the IPN is sufficient to explain most of the behavioral variability we observe. We do not feel the need to explore variations in metabolic activities, which are (by the way) very expensive experiments. However, we have added a sentence in the discussion to mention metabolic variabilities as a potential source of variability in nicotine consumption.

2) Av mice exposed to nicotine_200ug/ml display minimal nicotine_50ug/ml consumption, yet would Av mice restore a percent nicotine consumption >20 when exposed to a more extended session at 50ug/kg? Such a data set will help identify and isolate learned avoidance processes from dose-dependent avoidance behaviors.

We have now performed an additional two-bottle choice experiment to examine an extended time at 50 µg/ml. But we also performed the experiment a little differently. We directly proposed a high nicotine concentration to mice (200 µg/ml), followed by 8 days at 50 µg/ml. We found that, overall, mice avoided the 200 µg/ml nicotine solution, and that the following increase in nicotine preference was slow and gradual throughout the eight days at 50 µg/ml (Figure 2-figure supplement 1C). This slow adjustment to a lower-dose contrasts with the rapid (within a day) change in intake observed when nicotine concentration increases (Figure 1-figure supplement 1A). About half of the mice (6/13) retained a steady, low nicotine preference (< 20%) throughout the eight days at 50 µg/ml, resembling what was observed for avoiders in Figure 2D. Together, these results suggest that some of the mice, the non-avoiders, rapidly adjust their intake to adapt to changes in nicotine concentration in the bottle. For avoiders, aversion for nicotine seems to involve a learning mechanism that, once triggered, results in prolonged cessation of nicotine consumption.

3) The author should further investigate the basal properties of IPn neuron in vivo firing rate activity recorded and establish if their spontaneous activity determines their nicotine responses in vivo, such as firing rate, ISI, tonic, or phasic patterns. These analyses will provide helpful information to the neurophysiologist investigating the function of IPn neurons and will also inform how chronic nicotine exposure shapes the IPn neurophysiological properties.

We have performed additional analyses of the in vivo recordings. First, we have built maps of the recorded neurons, and we show that there is no anatomical bias in our sampling between the different groups. The only condition for which we did not sample neurons similarly is when we compare the responses to nicotine in vivo in WT and b4-/- mice (Figure 4E). The two groups were not distributed similarly along the dorso-ventral axis (Figure 4-figure supplement 2B). Yet, we do not think that the difference in nicotine responses observed between WT and b4-/- mice is due to a sampling bias. Indeed, we found no link between the response to nicotine and the dorsoventral coordinates of the neurons, in any of the groups (MPNic and MP Sal in Figure 3-figure supplement 1D; WT and b4-/- mice in Figure 4-figure supplement 2C). Therefore, our different groups are directly comparable, and the conclusions drawn in our study fully justified.

As requested, we have looked at whether the basal firing rate of IPN neurons determines the response to nicotine and indeed, neurons with higher firing rate show greater change in firing frequency upon nicotine injection (Figure 3 -figure supplement 1G and Figure 4-figure supplement 2F). We have also looked at the effect of chronic nicotine on the spontaneous firing rate of IPN neurons (Figure 3 -figure supplement 1F) but found no evidence for a change in basal firing properties. Similarly, the deletion of b4 had no effect on the spontaneous activity of the recorded neurons (Figure 4-figure supplement 2F). Finally, we found no evidence for any link between the anatomical coordinates of the neurons and their basal firing rate (Figure 3-figure supplement 1E and Figure 4figure supplement 2D).

Reviewer #3 (Public Review):

The manuscript by Mondoloni et al characterizes two-bottle choice oral nicotine consumption and associated neurobiological phenotypes in the antiparticle nucleus (IPN) using mice. The paper shows that mice exhibit differential oral nicotine consumption and correlate this difference with nicotine-evoked inward currents in neurons of the IPN. The beta4 nAChR subunit is likely involved in these responses. The paper suggests that prolonged exposure to nicotine results in reduced nAChR functional responses in IPN neurons. Many of these results or phenotypes are reversed or reduced in mice that are null for the beta4 subunit. These results are interesting and will add a contribution to the literature. However, there are several major concerns with the nicotine exposure model and a few other items that should be addressed.

Strengths:

Technical approaches are well-done. Oral nicotine, electrophysiology, and viral re-expression methods were strong and executed well. The scholarship is strong and the paper is generally well-written. The figures are high-quality.

We would like to thank the reviewer for his/her comments and suggestions on how to improve the manuscript.

Weaknesses:

Two bottle choice (2BC) model. 2BC does not examine nicotine reinforcement, which is best shown as a volitional preference for the drug over the vehicle. Mice in this 2BC assay (and all such assays) only ever show indifference to nicotine at best - not preference. This is seen in the maximal 50% preference for the nicotine-containing bottle. 2BC assays using tastants such as saccharin are confounded. Taste responses can very likely differ from primary reinforcement and can be related to peripheral biology in the mouth/tongue rather than in the brain reward pathway.

The two-bottle nicotine drinking test is a commonly used method to study addiction in mice (Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319). Like all methods, it has its limitations, but it also allows for different aspects to be addressed than those covered by selfadministration protocols. The two-bottle nicotine drinking test simply measures the animals' preference for a solution containing nicotine over a control solution without nicotine: the animals are free to choose nicotine or not, which allows to evaluate sensitivity and avoidance thresholds. What we show in this paper is precisely that despite interindividual differences in the way the drug is used (passively or actively), a significant proportion of the animals avoids the nicotine bottle at a certain concentration, suggesting that we are dealing with individual characteristics that are interesting to identify in the context of addiction and vulnerability. We agree that the twobottle choice test cannot provide as much information about the reinforcing effects of the drug as selfadministration procedures. We are aware of the limitations of the method and were careful not to interpret our data in terms of reinforcement to the drug. For instance, mice that consume nicotine were called “non-avoiders” and not “consumers”. We added a few sentences at the beginning of the discussion to highlight these limitations.

The reviewer states that the mice in this 2BC assay (and all such assays) “only ever show indifference to nicotine at best - not preference”. This is seen in the maximal 50% preference for the nicotine-containing bottle. While this is true on average, it isn’t when we look at individual profiles, as we did here. We clearly observed that some mice have a strong preference for nicotine and, conversely, that some mice actively avoid nicotine after a certain concentration is proposed in the bottle.

Regarding tastants, we indeed used saccharine to hide the bitter taste of nicotine and prevent taste-related side bias. This is a classical (though not perfect) paradigm in the field of nicotine research (Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319). To evaluate whether different sensitivities to the bitterness of nicotine may explain the interindividual differences in nicotine consumption we performed new experiments (as suggested by all three reviewers). In this two-bottle choice experiment, mice were first proposed a high concentration of nicotine (100 µg/ml) which has previously been shown to induce avoidance behavior in mice (Figure 3C). Then, mice were offered three increasing concentrations of quinine: 30, 100 and 300 µM. Quinine avoidance was dose dependent, as expected: it was moderate for 30 µM but almost absolute for 300 µM quinine. We then investigated whether nicotine and quinine avoidances were linked. We found no correlation between nicotine and quinine preference (new Figure: Figure 1- supplementary figure 1D). This new experiment strongly suggests that aversion to the drug is not directly tied to the sensitivity of mice to the bitter taste of nicotine. Other results reinforce this conclusion. First, none of the b4-/- mice (0/13) showed aversion to nicotine, whereas about half of the virally-rescued animals (8/17, b4 re-expressed in the IPN of b4-/- mice) showed nicotine aversion, a proportion similar to the one observed in WT mice. This experiment makes a clear, direct link between the expression of b4 nAChRs in the IPN and aversion to the drug. Furthermore, we also verified that the sensitivity of b4-/- mice to bitterness is not different from that of WT mice (new Figure 4 - figure supplement 1B). This new result indicates that the reason why b4-/- mice consume more nicotine than WT mice is not because they have a reduced sensitivity bitterness. Together, these new experiments strongly suggests that interindividual differences in sensitivity to the bitterness of nicotine play little role in nicotine consumption behavior in mice.

Moreover, this assay does not test free choice, as nicotine is mixed with water which the mice require to survive. Since most concentrations of nicotine are aversive, this may create a generalized conditioned aversion to drinking water - detrimental to overall health and a confounding factor.

Mice are given a choice between two bottles, only one of which contains nicotine. Hence, even though their choices are not fully free (they are being presented with a limited set of options), mice can always decide to avoid nicotine and drink from the bottle containing water only. We do not understand how this situation may create a generalized aversion to drinking. In fact, we have never observed any mouse losing weight or with deteriorated health condition in this test, so we don’t think it is a confounding factor.

What plasma concentrations of nicotine are achieved by 2BC? When nicotine is truly reinforcing, rodents and humans titrate their plasma concentrations up to 30-50 ng/mL. The Discussion states that oral self-administration in mice mimics administration in human smokers (lines 388-389). This is unjustified and should be removed. Similarly, the paragraph in lines 409-423 is quite speculative and difficult or impossible to test. This paragraph should be removed or substantially changed to avoid speculation. Overall, the 2BC model has substantial weaknesses, and/or it is limited in the conclusions it will support.

The reviewer must have read another version of our article, because these sentences and paragraphs are not present in our manuscript.

Regarding the actual concentration of nicotine in the plasma, this is indeed a good question. We have actually measured the plasma concentrations of nicotine for another study (article in preparation). The results from this experiment can be found below. The half-life of nicotine is very short in the blood and brain of mice (about 6 mins, see Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319), making it very hard to assess. Therefore, we also assessed the plasma concentration of cotinine, the main metabolite of nicotine. We compared 4 different conditions: home-cage (forced drinking of 100 ug/ml nicotine solution); osmotic minipump (OP, 10 mg/kg/d, as in our current study); Souris-city (a large social environment developed by our group, see Torquet et al. Nat. Comm. 2018); and the two-bottle choice procedure (when a solution of nicotine 100 ug/ml was proposed). The concentrations of plasma nicotine found were very low for all groups that drank nicotine, but not for the group that received nicotine through the osmotic minipump group. This is most likely because mice did not drink any nicotine in the hour prior to being sampled and all nicotine was metabolized. Indeed, when we look at the plasma concentration of cotinine, we see that cotinine was present in all of the groups. The plasma concentration of cotinine was similar in the groups for which “consumption” was forced: forced drinking in the home cage (HC) or infusion through osmotic minipump. This indicates that the plasma concentration of cotinine is similar whether mice drink nicotine (100 ug/ml) or whether nicotine is infused with the minipump (10 mg/kg/d). For Souris city and the two-bottle choice procedure, the cotinine concentrations were in the same range (mostly between 0-100 ng/ml). Globally, the concentrations of nicotine and cotinine found in the plasma of mice that underwent the two-bottle choice procedure are in the range of what has been previously described (Matta, S. G. et al. 2006. Guidelines on nicotine dose selection for in vivo research. Psychopharmacology 190, 269–319).

Regarding the limitations of the two-bottle choice test, we discuss them more extensively in the current version of the manuscript.

Statistical testing on subgroups. Mice are run through an assay and assigned to subgroups based on being classified as avoiders or non-avoiders. The authors then perform statistical testing to show differences between the avoiders and non-avoiders. It is circular to do so. When the authors divided the mice into avoiders and non-avoiders, this implies that the mice are different or from different distributions in terms of nicotine intake. Conducting a statistical test within the null hypothesis framework, however, implies that the null hypothesis is being tested. The null hypothesis, by definition, is that the groups do NOT differ. Obviously, the authors will find a difference between the groups in a statistical test when they pre-sorted the mice into two groups, to begin with. Comparing effect sizes or some other comparison that does not invoke the null hypothesis would be appropriate.

Our analysis, which can be summarized as follows, is fairly standard (see Krishnan, V. et al. (2007) Molecular adaptations underlying susceptibility and resistance to social defeat in brain reward regions. Cell 131, 391–404). Firstly, the mice are segregated into two groups based on their consumption profile, using the variability in their behavior. The two groups are obviously statistically different when comparing their consumption. This first analytical step allows us to highlight the variability and to establish the properties of each sub-population in terms of consumption. Our analysis could support the reviewer's comment if it ended at this point. However, our analysis doesn't end here and moves on to the second step. The separation of the mice into two groups (which is now a categorical variable) is used to compare the distribution of other variables, such as mouse choice strategy and current amplitude, based on the 2 categories. The null hypothesis tested is that the value of these other variables is not different between groups. There is no a priori obvious reason for the currents recorded in the IPN to be different in the two groups. These approaches allow us to show correlations between the variables. Finally, in the third and last step, one (or several) variable(s) are manipulated to check whether nicotine consumption is modified accordingly. Manipulation was performed by exposing mice to chronic nicotine, by using mutant mice with decreased nicotinic currents, and by re-expressing the deleted nAChR subunit only in the IPN. This procedure is fairly standard, and cannot be considered as a circular analysis with data selection problem, as explained in (Kriegeskorte, N., Simmons, W. K., Bellgowan, P. S. F. & Baker, C. I. (2009) Circular analysis in systems neuroscience: the dangers of double dipping. Nature Neuroscience 12, 535-540).

Decreased nicotine-evoked currents following passive exposure to nicotine in minipumps are inconsistent with published results showing that similar nicotine exposure enhances nAChR function via several measures (Arvin et al, J Neurosci, 2019). The paper does acknowledge this previous paper and suggests that the discrepancy is explained by the fact that they used a higher concentration of nicotine (30 uM) that was able to recruit the beta4containing receptor (whereas Arvin et al used a caged nicotine that was unable to do so). This may be true, but the citation of 30 uM nicotine undercuts the argument a bit because 30 uM nicotine is unlikely to be achieved in the brain of a person using tobacco products; nicotine levels in smokers are 100-500 nM. It should be noted in the paper that it is unclear whether the down-regulated receptors would be active at concentrations of nicotine found in the brain of a smoker.

We indeed find opposite results compared to Arvin et al., and we give possible explanations for this discrepancy in the discussion. To be honest we don’t fully understand why we have opposite results. However, we clearly observed a decreased response to nicotine, both in vitro (with 30 µM nicotine on brain slices) and in vivo (with a classical dose of 30 µg/kg nicotine i.v.), while Arvin et al. only tested nicotine in vitro.

Regarding the reviewer’s comment about the nicotine concentration used (30 µM): we used that concentration in vitro to measure nicotine-induced currents (it’s a concentration close to the EC50 for heteromeric receptors, which will likely recruit low affinity a3b4 receptors) and to evaluate the changes in nAChR current following nicotine exposure. We did not use that concentration to induce nAChR desensitization, so we don’t really understand the argument regarding the levels of nicotine in smokers. For inducing desensitization, we used a minipump that delivers a daily dose of 10 mg/kg/day, which is the amount of nicotine mice drink in our assay.

The statement in lines 440-41 ("we show that concentrations of nicotine as low as 7.5 ug/kg can engage the IPN circuitry") is misleading, as the concentration in the water is not the same as the concentration in the CSF since the latter would be expected to build up over time. The paper did not provide measurements of nicotine in plasma or CSF, so concluding that the water concentration of nicotine is related to plasma concentrations of nicotine is only speculative.

The sentence “we show that concentrations of nicotine as low as 7.5 ug/kg can engage the IPN circuitry" is not in the manuscript so the reviewer must have read another version of the paper.

The results in Figure 2E do not appear to be from a normal distribution. For example, results cluster at low (~100 pA) responses, and a fraction of larger responses drive the similarities or differences.

Indeed, that is why we performed a non-parametric Mann-Whitney test for comparing the two groups, as indicated in the legend of figure 2E.

10 mg/kg/day in mice or rats is likely a non-physiological exposure to nicotine. Most rats take in 1.0 to 1.5 mg/kg over a 23-hour self-administration period (O'Dell, 2007). Mice achieve similar levels during SA (Fowler, Neuropharmacology 2011). Forced exposure to 10 mg/kg/day is therefore 5 to 10-fold higher than rodents would ever expose themselves to if given the choice. This should be acknowledged in a limitations section of the Discussion.

The two-bottle choice task is very different from nicotine self-administration procedures in terms of administration route: oral versus injected (in the blood or in the brain), respectively. Therefore, the quantities of drug consumed cannot be directly compared. In our manuscript, mice consume on average 10 mg/kg/day of nicotine at the highest nicotine concentration tested, which is fully consistent with what was already published in many studies (20 mg/kg/day in Frahm et al. Neuron 2013, 5-10 mg/kg/day in Bagdas et al., NP 2020, 10-20 mg/kg/day in Bagdas et al. NP2019, to cite a few...). Hence, we used that concentration of nicotine (10 mg/kg/d) for chronic administration of nicotine using minipumps. This is also a nicotine concentration that is classically used in osmotic minipumps for chronic administration of nicotine: 10 mg/kg/d in Dongelmans et al. Nat. Com 2021 (our lab), 12 mg/kg/d in Arvin et al. J. Neuro. 2019 (Drenan lab), 12 mg/kg/d in Lotfipour et al. J. Neuro. 2013 (Boulter lab) etc… Therefore, we do not see the issue here.

Are the in vivo recordings in IPN enriched or specific for cells that have a spontaneous firing at rest? If so, this may or may not be the same set/type of cells that are recorded in patch experiments. The results could be biased toward a subset of neurons with spontaneous firing. There are MANY different types of neurons in IPN that are largely intermingled (see Ables et al, 2017 PNAS), so this is a potential problem.

It is true that there are many types of neurons in the IPN. In-vivo electrophysiology and slice electrophysiology should be considered as two complementary methods to obtain detailed properties of IPN neurons. The populations sampled by these two methods are certainly not identical (IPR in patch -clamp versus mostly IPR and IPC in vivo), and indeed only spontaneously active neurons are recorded in in-vivo electrophysiology. The question is whether this is or not a potential problem. The results we obtained using in-vivo and brain-slice electrophysiology are consistent (i.e., a decreased response to nicotine), which indicates that our results are robust and do not depend on the selection of a particular subpopulation. In addition, we now provide the maps of the neurons recorded both in slices and in vivo (see supplementary figures, and response to the other two referees). We show that, overall, there is no bias sampling between the different groups. Together, these new analyses strongly suggest that the differences we observe between the groups are not due to sampling issues. We have added the Ables 2017 reference and are discussing neuron variability more extensively in the revised manuscript.

Related to the above issue, which of the many different IPN neuron types did the group re-express beta4? Could that be controlled or did beta4 get re-expressed in an unknown set of neurons in IPN? There is insufficient information given in the methods for verification of stereotaxic injections.

Re-expression of b4 was achieved with a strong, ubiquitous promoter (pGK), hence all cell types should in principle be transduced. This is now clearly stated in the result section, the figure legend and the method section. Unfortunately, we had no access to a specific mouse line to restrict expression of b4 to b4-expressing cells, since the b4-Cre line of GENSAT is no more alive. This mouse line was problematic anyways because expression levels of the a3, a5 and b4 nAChR subunits, which belong to the same gene cluster, were reported to be affected. Yet, we show in this article that deleting b4 leads to a strong reduction of nicotine-induced currents in the IPR (80%, patch-clamp), and of the response to nicotine in vivo (65%). These results indicate that b4 is strongly expressed in the IPN, likely in a large majority of IPR and IPC neurons (see also our response to reviewer 1). In addition, we show that our re-expression strategy restores nicotine-induced currents in patch-clamp experiments and also the response to nicotine in vivo (new Figure 5C). Non-native expression levels could potentially be achieved (e.g. overexpression) but this is not what we observed: responses to nicotine were restored to the WT levels (in slices and in vivo). And importantly this strategy rescued the WT phenotype in terms of nicotine consumption. Expression of b4 alone in cells that do not express any other nAChR subunit (as, presumably, in the lateral parts of the IPN, see GENSAT images above) should not produce any functional nAChR, since alpha subunits are mandatory to produce functional receptors. As specified in the manuscript, proper transduction of the IPN was verified using post-hoc immunochemistry, and mice with transduction of b4 in the VTA were excluded from the analyses.

Data showing that alpha3 or beta4 disruption alters MHb/IPN nAChR function and nicotine 2BC intake is not novel. In fact, some of the same authors were involved in a paper in 2011 (Frahm et al., Neuron) showing that enhanced alpha3beta4 nAChR function was associated with reduced nicotine consumption. The present paper would therefore seem to somewhat contradict prior findings from members of the research group.

Frahm et al used a transgenic mouse line (called TABAC) in which the expression of a3b4 receptor is increased, and they observed reduced nicotine consumption. We do the exact opposite: we reduce (a3)b4 receptor expression (using the b4 knock-out line, or by putting mice under chronic nicotine), and observe increased consumption. There is thus no contradiction. In fact, we discuss our findings in the light of Frahm et al. in the discussion section.

Sex differences. All studies were conducted in male mice, therefore nothing was reported regarding female nicotine intake or physiology responses. Nicotine-related biology often shows sex differences, and there should be a justification provided regarding the lack of data in females. A limitations section in the Discussion section is a good place for this.

We agree with the reviewer. We added a sentence in the discussion.

Author Response

Reviewer #1 (Public Review):

1) Although I found the introduction well written, I think it lacks some information or needs to develop more on some ideas (e.g., differences between the cerebellum and cerebral cortex, and folding patterns of both structures). For example, after stating that "Many aspects of the organization of the cerebellum and cerebrum are, however, very different" (1st paragraph), I think the authors need to develop more on what these differences are. Perhaps just rearranging some of the text/paragraphs will help make it better for a broad audience (e.g., authors could move the next paragraph up, i.e., "While the cx is unique to mammals (...)").

We have added additional context to the introduction and developed the differences between cerebral and cerebellar cortex, also re-arranging the text as suggested.

2) Given that the authors compare the folding patterns between the cerebrum and cerebellum, another point that could be mentioned in the introduction is the fact that the cerebellum is convoluted in every mammalian species (and non-mammalian spp as well) while the cerebrum tends to be convoluted in species with larger brains. Why is that so? Do we know about it (check Van Essen et al., 2018)? I think this is an important point to raise in the introduction and to bring it back into the discussion with the results.

We now mention in the introduction the fact that the cerebellum is folded in mammals, birds and some fishes, and provide references to the relevant literature. We have also expanded our discussion about the reasons for cortical folding in the discussion, which now contains a subsection addressing the subject (this includes references to the work of Van Essen).

3) In the results, first paragraph, what do the authors mean by the volume of the medial cerebellum? This needs clarification.

We have modified the relevant section in the results, and made the definition of the medial cerebellum more clear indicating that we refer to the vermal region of the cerebellum.

4) In the results: When the authors mention 'frequency of cerebellar folding', do they mean the degree of folding in the cerebellum? At least in non-mammalian species, many studies have tried to compare the 'degree or frequency of folding' in the cerebellum by different proxies/measurements (see Iwaniuk et al., 2006; Yopak et al., 2007; Lisney et al., 2007; Yopak et al., 2016; Cunha et al., 2022). Perhaps change the phrase in the second paragraph of the result to: "There are no comparative analyses of the frequency of cerebellar folding in mammals, to our knowledge".

We have modified the subsection in the methods referring to the measurement of folial width and folial perimeter to make the difference more clear. The folding indices that have been used previously (which we cite) are based on Zilles’s gyrification index. This index provides only a global idea of degree of folding, but it’s unable to distinguish a cortex with profuse shallow folds from one with a few deep ones. An example of this is now illustrated in Fig. 3d, where we also show how that problem is solved by the use of our two measurements (folial width and perimeter). The problem is also discussed in the section about the measurement of folding in the discussion section:

“Previous studies of cerebellar folding have relied either on a qualitative visual score (Yopak et al. 2007, Lisney et al. 2008) or a “gyrification index” based on the method introduced by Zilles et al. (1988, 1989) for the study of cerebral folding (Iwaniuk et al. 2006, Cunha et al. 2020, 2021). Zilles’s gyrification index is the ratio between the length of the outer contour of the cortex and the length of an idealised envelope meant to reflect the length of the cortex if it were not folded. For instance, a completely lissencephalic cortex would have a gyrification index close to 1, while a human cerebral cortex typically has a gyrification index of ~2.5 (Zilles et al. 1988). This method has certain limitations, as highlighted by various researchers (Germanaud et al. 2012, 2014, Rabiei et al. 2018, Schaer et al. 2008, Toro et al. 2008, Heuer et al. 2019). One important drawback is that the gyrification index produces the same value for contours with wide variations in folding frequency and amplitude, as illustrated in Fig. 3d. In reality, folding frequency (inverse of folding wavelength) and folding amplitude represent two distinct dimensions of folding that cannot be adequately captured by a single number confusing both dimensions. To address this issue we introduced 2 measurements of folding: folial width and folial perimeter. These measurements can be directly linked to folding frequency and amplitude, and are comparable to the folding depth and folding wavelength we introduced previously for cerebral 3D meshes (Heuer et al. 2019). By using these measurements, we can differentiate folding patterns that could be confused when using a single value such as the gyrification index (Fig. 3d). Additionally, these two dimensions of folding are important, because they can be related to the predictions made by biomechanical models of cortical folding, as we will discuss now.”

5) Sultan and Braitenberg (1993) measured cerebella that were sagittally sectioned (instead of coronal), right? Do you think this difference in the plane of the section could be one of the reasons explaining different results on folial width between studies? Why does the foliation index calculated by Sultan and Braitenberg (1993) not provide information about folding frequency?

The measurement of foliation should be similar as far as enough folds are sectioned perpendicular to their main axis. This will be the case for folds in the medial cerebellum (vermis) sectioned sagittally, and for folds in the lateral cerebellum sectioned coronally. The foliation index of Sultan and Braitenberg does not provide a similar account of folding frequency as we do because they only measure groups of folia (what some called lamellae), whereas we measure individual folia. It is not easy to understand exactly how Sultan and Braitenberg proceeded from their paper. We contacted Prof. Fahad Sultan (we acknowledge his help in our manuscript). Author response image 1 provides a more clear description of their procedure:

Author response image 1.

As Author response image 1 shows, each of the structures that they call a fold is composed of several folia, and so their measurements are not comparable with ours which measure individual folia (a). The flattened representation (b) is made by stacking the lengths of the fold axes (dashed lines), separating them by the total length of each fold (the solid lines), which each may contain several folia.

6) Another point that needs to be clarified is the log transformation of the data. Did the authors use log-transformed data for all types of analyses done in the study? Write this information in the material and methods.

Yes, we used the log10 transformation for all our measurements. This is now mentioned in the methods section, and again in the section concerning allometry. We are including a link to all our code to facilitate exact replication of our entire method, including this transformation.

7) The discussion needs to be expanded. The focus of the paper is on the folding pattern of the cerebellum (among different mammalian species) and its relationship with the anatomy of the cerebrum. Therefore, the discussion on this topic needs to be better developed, in my opinion (especially given the interesting results of this paper). For example, with the findings of this study, what can we say about how the folding of the cerebellum is determined across mammals? The authors found that the folial width, folial perimeter, and thickness of the molecular layer increase at a relatively slow rate across the species studied. Does this mean that these parameters have little influence on the cerebellar folding pattern? What mostly defines the folding patterns of the cerebellum given the results? Is it the interaction between section length and area? Can the authors explain why size does not seem to be a "limiting factor" for the folding of the cerebellum (for example, even relatively small cerebella are folded)? Is that because the 'white matter' core of the cerebellum is relatively small (thus more stress on it)?

We have expanded the discussion as suggested, with subsections detailing the measuring of folding, the modelling of folding for the cerebrum and the cerebellum, and the role that cerebellar folding may play in its function. We refer to the literature on cortical folding modelling, and we discuss our results in terms of the factors that this research has highlighted as critical for folding. From the discussion subsection on models of cortical folding:

“The folding of the cerebral cortex has been the focus of intense research, both from the perspective of neurobiology (Borrell 2018, Fernández and Borrell 2023) and physics (Toro and Burnod 2005, Tallinen et al. 2014, Kroenke and Bayly 2018). Current biomechanical models suggest that cortical folding should result from a buckling instability triggered by the growth of the cortical grey matter on top of the white matter core. In such systems, the growing layer should first expand without folding, increasing the stress in the core. But this configuration is unstable, and if growth continues stress is released through cortical folding. The wavelength of folding depends on cortical thickness, and folding models such as the one by Tallinen et al. (2014) predict a neocortical folding wavelength which corresponds well with the one observed in real cortices. Tallinen et al. (2014) provided a prediction for the relationship between folding wavelength λ and the mean thickness (𝑡) of the cortical layer: λ = 2π𝑡(µ/(3µ𝑠))1/3. (...)”

From this biomechanical framework, our answers to the questions of the Reviewer would be:

• How is the folding of the cerebellum determined across mammals? By the expansion of a layer of reduced thickness on top of an elastic layer (the white matter)

• Folial width, folial perimeter, and thickness of the molecular layer increase at a relatively slow rate across the species studied. Does this mean that these parameters have little influence on the cerebellar folding pattern? On the contrary, that indicates that the shape of individual folia is stable, providing the smallest level of granularity of a folding pattern. In the extreme case where all folia had exactly the same size, a small cerebellum would have enough space to accommodate only a few folia, whereas a large cerebellum would accommodate many more.

• What mostly defines the folding patterns of the cerebellum given the results? Is it the interaction between section length and area? It’s the mostly 2D expansion of the cerebellar cortical layer and its thickness.

• Can the authors explain why size does not seem to be a "limiting factor" for the folding of the cerebellum? Because even a cerebellum of very small volume would fold if its cortex were thin enough and expanded sufficiently. That’s why the cerebellum folds even while being smaller than the cerebrum: because its cortex is much thinner.

8) One caveat or point to be raised is the fact that the authors use the median of the variables measured for the whole cerebellum (e.g., median width and median perimeter across all folia). Although the cerebellum is highly uniform in its gross internal morphology and circuitry's organization across most vertebrates, there is evidence showing that the cerebellum may be organized in different functional modules. In that way, different regions or folia of the cerebellum would have different olivo-cortico-nuclear circuitries, forming, each one, a single cerebellar zone. Although it is not completely clear how these modules/zones are organized within the cerebellum, I think the authors could acknowledge this at the end of their discussion, and raise potential ideas for future studies (e.g., analyse folding of the cerebellum within the brain structure - vermis vs lateral cerebellum, for example). I think this would be a good way to emphasize the importance of the results of this study and what are the main questions remaining to be answered. For example, the expansion of the lateral cerebellum in mammals is suggested to be linked with the evolution of vocal learning in different clades (see Smaers et al., 2018). An interesting question would be to understand how foliation within the lateral cerebellum varies across mammalian clades and whether this has something to do with the cellular composition or any other aspect of the microanatomy as well as the evolution of different cognitive skills in mammals.

We now address this point in a subsection of the discussion which details the implications of our methodological decisions and the limitations of our approach. It is true that the cerebellum is regionally variable. Our measurements of folial width, folial perimeter and molecular layer thickness are local, and we should be able to use them in the future to study regional variation. However, this comes with a number of difficulties. First, it would require sampling all the cerebellum (and the cerebrum) and not just one section. But even if that were possible that would increase the number of phenotypes, beyond the current scope of this study. Our central question about brain folding in the cerebellum compared to the cerebrum is addressed by providing data for a substantial number of mammalian species. As indicated by Reviewer #3, adding more variables makes phylogenetic comparative analyses very difficult because the models to fit become too large.

Reviewer #2 (Public Review):

1) The methods section does not address all the numerical methods used to make sense of the different brain metrics.

We now provide more detailed descriptions of our measurements of foliation, phylogenetic models, analysis of partial correlations, phylogenetic principal components, and allometry. We have added illustrations (to Figs. 3 and 5), examples and references to the relevant literature.

2) In the results section, it sometimes makes it difficult for the reader to understand the reason for a sub-analysis and the interpretation of the numerical findings.

The revised version of our manuscript includes motivations for the different types of analyses, and we have also added a paragraph providing a guide to the structure of our results.

3) The originality of the article is not sufficiently brought forward:

a) the novel method to detect the depth of the molecular layer is not contextualized in order to understand the shortcomings of previously-established methods. This prevents the reader from understanding its added value and hinders its potential re-use in further studies.

The revised version of the manuscript provides additional context which highlights the novelty of our approach, in particular concerning the measurement of folding and the use of phylogenetic comparative models. The limitations of the previous approaches are stated more clearly, and illustrated in Figs. 3 and 5.

b) The numerous results reported are not sufficiently addressed in the discussion for the reader to get a full grasp of their implications, hindering the clarity of the overall conclusion of the article.

Following the Reviewer’s advice, we have thoroughly restructured our results and discussion section.

Reviewer #3 (Public Review):

1) The first problem relates to their use of the Ornstein-Uhlenbeck (OU) model: they try fitting three evolutionary models, and conclude that the Ornstein-Uhlenbeck model provides the best fit. However, it has been known for a while that OU models are prone to bias and that the apparent superiority of OU models over Brownian Motion is often an artefact, a problem that increases with smaller sample sizes. (Cooper et al (2016) Biological Journal of the Linnean Society, 2016, 118, 64-77).

Cooper et al.’s (2016) article “A Cautionary Note on the Use of Ornstein Uhlenbeck Models in Macroevolutionary Studies” suggests that comparing evolutionary models using the model’s likelihood leads often to incorrectly selecting OU over BM even for data generated from a BM process. However, Grabowski et al (2023) in their article ‘A Cautionary Note on “A Cautionary Note on the Use of Ornstein Uhlenbeck Models in Macroevolutionary Studies”’ suggest that Cooper et al.’s (2016) claim may be misleading. The work of Clavel et al. (2019) and Clavel and Morlon (2017) shows that the penalised framework implemented in mvMORPH can successfully recover the parameters of a multivariate OU process. To address more directly the concern of the Reviewer, we used simulations to evaluate the chances that we would decide for an OU model when the correct model was BM – a similar procedure to the one used by Cooper et al.’s (2016). However, instead of using the likelihood of the fitted models directly as Cooper et al. (2016) – which does not control for the number of parameters in the model – we used the Akaike Information Criterion, corrected for small sample sizes: AICc. The standard Akaike Information Criterion takes the number of parameters of the model into account, but this is not sufficient when the sample size is small. AICc provides a score which takes both aspects into account: model complexity and sample size. This information has been added to the manuscript:

“We selected the best fitting model using the Akaike Information Criterion (AIC), corrected for 𝐴𝐼𝐶 = − 2 𝑙𝑜𝑔(𝑙𝑖𝑘𝑒𝑙𝑖ℎ𝑜𝑜𝑑) + 2 𝑝. This approximation is insufficient when the𝑝 sample size small sample sizes (AICc). AIC takes into account the number of parameters in the model: is small, in which case an additional correction is required, leading to the corrected AIC: 𝐴𝐼𝐶𝑐 = 𝐴𝐼𝐶 + (2𝑝2 + 2𝑝)/(𝑛 − 𝑝 − 1), where 𝑛 is the sample size.”

In 1000 simulations of 9 correlated multivariate traits for 56 species (i.e., 56*9 data points) using our phylogenetic tree, only 0.7% of the times we would decide for OU when the real model was BM.

2) Second, for the partial correlations (e.g. fig 7) and Principal Components (fig 8) there is a concern about over-fitting: there are 9 variables and only 56 data points (violating the minimal rule of thumb that there should be >10 observations per parameter). Added to this, the inclusion of variables lacks a clear theoretical rationale. The high correlations between most variables will be in part because they are to some extent measuring the same things, e.g. the five different measures of cerebellar anatomy which include two measures of folial size. This makes it difficult to separate their effects. I get that the authors are trying to tease apart different aspects of size, but in practice, I think these results (e.g. the presence of negative coefficients in Fig 7) are really hard or impossible to interpret. The partial correlation network looks like a "correlational salad" rather than a theoretically motivated hypothesis test. It isn't clear to me that the PC analyses solve this problem, but it partly depends on the aims of these analyses, which are not made very clear.

PCA is simply a rigid rotation of the data, distances among multivariate data points are all conserved. Neither our PCA nor our partial correlation analysis involve model fitting, the concept of overfitting does not apply. PCA and partial correlations are also not used here for hypothesis testing, but as exploratory methods which provide a transformation of the data aiming at capturing the main trends of multivariate change. The aim of our analysis of correlation structure is precisely to avoid the “correlational salad” that the Reviewer mentions. The Reviewer is correct: all our variables are correlated to a varying degree (note that there are 56 data points per variable = 56*9 data points, not just 56 data points). Partial correlations and PCA aim at providing a principled way in which correlated measurements can be explored. In the revised version of the manuscript we include a more detailed description of partial correlations and PCA (phylogenetic). Whenever variables measure the same thing, they will be combined into the same principal component (these are the combinations shown in Fig. 8 b and d). Additionally, two variables may be correlated because of their correlation with a third variable (or more). Partial correlations address this possibility by looking at the correlations between the residuals of each pair of variables after all other variables have been covaried out. We provide a simple example which should make this clear, providing in particular an intuition for the meaning of negative correlations:

“All our phenotypes were strongly correlated. We used partial correlations to better understand pairwise relationships. The partial correlation between 2 vectors of measurements a and b is the correlation between their residuals after the influence of all other measurements has been covaried out. Even if the correlation between a and b is strong and positive, their partial correlation could be 0 or even negative. Consider, for example, 3 vectors of measurements a, b, c, which result from the combination of uncorrelated random vectors x, y, z. Suppose that a = 0.5 x + 0.2 y + 0.1 z, b = 0.5 x - 0.2 y + 0.1 z, and c = x. The measurements a and b will be positively correlated because of the effect of x and z. However, if we compute the residuals of a and b after covarying the effect of c (i.e., x), their partial correlation will be negative because of the opposite effect of y on a and b. The statistical significance of each partial correlation being different than 0 was estimated using the edge exclusion test introduced by Whittaker (1990).”

The rationale for our analyses has been made more clear in the revised version of the manuscript, aided by the more detailed description of our methods. In particular, we describe better the reason for our 2 measurements of folial shape – width and perimeter – which measure independent dimensions of folding (this is illustrated in Fig. 3d).

3) The claim of concerted evolution between cortical and cerebellar values (P 11-12) seems to be based on analyses that exclude body size and brain size. It, therefore, seems possible - or even likely - that all these analyses reveal overall size effects that similarly influence the cortex and cerebellum. When the authors state that they performed a second PC analysis with body and brain size removed "to better understand the patterns of neuroanatomical evolution" it isn't clear to me that is what this achieves. A test would be a model something like [cerebellar measure ~ cortical measure + rest of the brain measure], and this would deal with the problem of 'correlation salad' noted below.

The answer to this question is in the partial correlation diagram in Fig. 7c. This analysis does not exclude body weight nor brain weight. It shows that the strong correlation between cerebellar area and length is supported by a strong positive partial correlation, as is the link between cerebral area and length. There is a significant positive partial correlation between cerebellar section area and cerebral section length. That is, even after covarying everything else, there is still a correlation between cerebellar section area and cerebral section length (this partial correlation is equivalent to the suggestion of the Reviewer). Additionally, there is a positive partial correlation between body weight and cerebellar section area, but not significant partial correlation between body weight and cerebral section area or length. Our approach aims at obtaining a general view of all the relationships in the data. Testing an individual model would certainly decrease the number of correlations, however, it would provide only a partial view of the problem.

4) It is not quite clear from fig 6a that the result does indeed support isometry between the data sets (predicted 2/3 slope), and no coefficient confidence intervals are provided.

We have now added the numerical values of the CIs to all our plots in addition to the graphical representations (grey regions) in the previous version of the manuscript. The isometry slope (0.67) is either within the CIs (both for the linear and orthogonal regressions) or at the margin, indicating that if the relationships are not isometric, they are very close to it.

Referencing/discussion/attribution of previous findings

5) With respect to the discussion of the relationship between cerebellar architecture and function, and given the emphasis here on correlated evolution with cortex, Ramnani's excellent review paper goes into the issues in considerable detail, which may also help the authors develop their own discussion: Ramnani (2006) The primate cortico-cerebellar system: anatomy and function. Nature Reviews Neuroscience 7, 511-522 (2006)

We have added references to the work of Ramnani.

6) The result that humans are outliers with a more folded cerebellum than expected is interesting and adds to recent findings highlighting evolutionary changes in the hominin human cerebellum, cerebellar genes, and epigenetics. Whilst Sereno et al (2020) are cited, it would be good to explain that they found that the human cerebellum has 80% of the surface area of the cortex.

We have added this information to the introduction:

“In humans, the cerebellum has ~80% of the surface area of the cerebral cortex (Sereno et al. 2020), and contains ~80% of all brain neurons, although it represents only ~10% of the brain mass (Azevedo et al. 2009)”

7) It would surely also be relevant to highlight some of the molecular work here, such as Harrison & Montgomery (2017). Genetics of Cerebellar and Neocortical Expansion in Anthropoid Primates: A Comparative Approach. Brain Behav Evol. 2017;89(4):274-285. doi: 10.1159/000477432. Epub 2017 (especially since this paper looks at both cerebellar and cortical genes); also Guevara et al (2021) Comparative analysis reveals distinctive epigenetic features of the human cerebellum. PLoS Genet 17(5): e1009506. https://doi.org/10.1371/journal. pgen.1009506. Also relevant here is the complex folding anatomy of the dentate nucleus, which is the largest structure linking cerebellum to cortex: see Sultan et al (2010) The human dentate nucleus: a complex shape untangled. Neuroscience. 2010 Jun 2;167(4):965-8. doi: 10.1016/j.neuroscience.2010.03.007.

The information is certainly important, and could have provided a wider perspective on cerebellar evolution, but we would prefer to keep a focus on cerebellar anatomy and address genetics only indirectly through phylogeny.

8) The authors state that results confirm previous findings of a strong relationship between cerebellum and cortex (P 3 and p 16): the earliest reference given is Herculano-Houzel (2010), but this pattern was discovered ten years earlier (Barton & Harvey 2000 Nature 405, 1055-1058. https://doi.org/10.1038/35016580; Fig 1 in Barton 2002 Nature 415, 134-135 (2002). https://doi.org/10.1038/415134a) and elaborated by Whiting & Barton (2003) whose study explored in more detail the relationship between anatomical connections and correlated evolution within the cortico-cerebellar system (this paper is cited later, but only with reference to suggestions about the importance of functions of the cerebellum in the context of conservative structure, which is not its main point). In fact, Herculano-Houzel's analysis, whilst being the first to examine the question in terms of numbers of neurons, was inconclusive on that issue as it did not control for overall size or rest of the brain (A subsequent analysis using her data did, and confirmed the partially correlated evolution - Barton 2012, Philos Trans R Soc Lond B Biol Sci. 367:2097-107. doi: 10.1098/rstb.2012.0112.)

We apologise for this oversight, these references are now included.

Author Response

Reviewer #2 (Public Review):

The manuscript by Ma et al, "Two RNA-binding proteins mediate the sorting of miR223 from mitochondria into exosomes" examines the contribution of two RNA-binding proteins on the exosomal loading of miR223. The authors conclude that YBX1 and YBAP1 work in tandem to traffic and load miR223 into the exosome. The manuscript is interesting and potentially impactful. It proposes the following scenario regarding the exosomal loading of miR223: (1) YBAP1 sequesters miR223 in the mitochondria, (2) YBAP1 then transfers miR223 to YBX1, and (3) YBX1 then delivers miR223 into the early endosome for eventual secretion within an exosome. While the authors propose plausible explanations for this phenomenon, they do not specifically test them and no mechanism by which miR223 is shuttled between YBAP1 and YBX1, and the exosome is shown. Thus, the paper is missing critical mechanistic experiments that could have readily tested the speculative conclusions that it makes.

Comments:

1) The major limitation of this paper is that it fails to explore the mechanism of any of the major changes it describes. For example, the authors propose that miR223 shuttles from mitochondrially localized YBAP1 to P-body-associated YBX1 to the exosome. This needs to be tested directly and could be easily addressed by showing a transfer of miR223 from YBAP1 to YBX1 to the exosome.

Testing this idea using fluorescently labeled miR223 would indeed be an ideal experiment. However, miRNA imaging presents challenges. As reviewer 1 pointed out, and we have now confirmed, the atto-647 dye itself localizes to mitochondria. We will continue our efforts to identify a suitable fluorescent label for miR223in order to be in a position to evaluate the temporal relationship between mitochondrial and endosomal miR223.

2) If YBAP1 retains miR223 in mitochondria, what is the trigger for YBAP1 to release it and pass it off to YBX1? The authors speculate in their discussion that sequestration of mito-miR223 plays a "role in some structural or regulatory process, perhaps essential for mitochondrial homeostasis, controlled by the selective extraction of unwanted miRNA into RNA granules and further by secretion in exosomes...". This is readily testable by altering mitochondria dynamics and/or integrity.

A previous study has reported that YBAP1 can be released from mitochondria to the cytosol during HSV-1 infection (Song et al., 2021). However, due to restrictions, we are unable to conduct experiments using HSV to verify this condition. We attempted to induce mitochondrial stress by using different concentrations of CCCP, but we did not observe the release of YBAP1 from mitochondria after CCCP treatment. We speculate that not all mitochondrial stress conditions can trigger YBAP1 release. Investigating the mechanism of mito-miR223 release from mitochondria is one of our interests that we aim to explore in future studies.

3) Much of the miRNA RT-PCR analysis is presented as a ratio of exosomal/cellular. This particular analysis assumes that cellular miRNA is unaffected by treatments. For example, Figure 1a shows that the presence of exosomal miR223 is significantly reduced when YBX1 is knocked out. This analysis does not consider the possibility that YBX1-KO alters (up or down-regulates) intracellular miR223 levels. Should that be the case, the ratiometric analysis is greatly skewed by intracellular miRNA changes. It would be better to not only show the intracellular levels of the miRs but also normalize the miRNA levels to the total amount of RNA isolated or an irrelevant/unchanged miRNA.

Our previous publications demonstrated that miR223 levels are increased in YBX1-KO cells and decreased in exosomes derived from YBX1 KO cells. However, no significant changes were observed in miR190 levels (Liu et al., 2021; Shurtleff et al., 2016). The repeated data has been included in Figure 1a.

For the analysis of other miRNAs by RT-PCR, we assessed changes in intracellular and exosomal miRNA levels in the corresponding figures. In the qPCR analysis, miRNA levels were normalized to the total amount of RNA.

4) In figure 1, the authors show that in YBX1-KO cells, miR223 levels are decreased in the exosome. They further suggest this is because YBX1 binds with high affinity to miR223. This binding is compared to miR190 which the authors state is not enriched in the exosome. However, no data showing that miR190 is not present in the exosome is shown. A figure showing the amount of cellular and exosomal miR223 and 190 should be shown together on the same graph.

In previous publications we demonstrated that miR190 is not localized in exosomes and not significantly changed in YBX1 knockout (KO) cells and exosomes derived from YBX1 KO cells (Liu et al., 2021; Shurtleff et al., 2016). The repeated data has been included in Figure 1a.

5) Figure 2 Supplement 1 - As to determine the nucleotides responsible for interacting with YBX1, the authors made several mutations within the miR223 sequence. However, no explanation is given regarding the mutant sequences used or what the ratios mean. Mutant sequences need to be included. How do the authors conclude that UCAGU is important when the locations of the mutations are unclear? Also, the interpretation of this data would benefit from a binding affinity curve as shown in Fig 2C.

The ratio is of labeled miR223/unlabeled miR223 (wt and mutant). All mutant sequences of miR223 have been included in Figure 2 supplement 1.

6) While the binding of miR223mut to YBX1 is reduced, there is still significant binding. Does this mean that the 5nt binding motif is not exact? Do the authors know if there are multiple nucleotide possibilities at these positions that could facilitate binding? Perhaps confirming binding "in vivo" via RIP assay would further solidify the UCAGU motif as critical for binding to YBX1.

The binding affinity of miR223mut with YBX1 is reduced approximately 27-fold compared to miR223. We speculate that the secondary structure of miR223 may contribute to the interaction with YBX1.

Our EMSA data, in vitro packaging data, and exosome analysis reinforce the conclusion that UCAGU is critical for YBX1 binding. These findings suggest that the presence of the UCAGU motif in miR223 is crucial for its interaction with YBX1 and subsequent sorting into exosomes.

7) Figures 2g, h - It would be nice to show that miR190mut also packages in the cell-free system. This would confirm that the sequence is responsible. Also, to confirm that the sorting of miR223 is YBX1-dependent, a cell-free reaction using cytosol and membranes from YBX1 KO cells is needed.

Although we have not performed the suggested experiment, we purified exosomes from cells overexpressing miR190sort and observed an increase in the enrichment of miR190sort in exosomes compared to miR190. This finding confirmed that the UCAGU motif facilitates miRNA sorting into exosomes.

Regarding the in vitro packaging assay, our previously published paper demonstrated that cytosol from YBX1 knockout (KO) cells significantly reduces the protection of miR223 from RNase digestion. We concluded that the sorting of miR223 into exosomes is dependent on YBX1 (Shurtleff et al., 2016).

8) In Figure 3a, the authors show that miR223 is mitochondrially localized. Does the sequence of miR223 (WT or Mut) matter for localization? Does it matter for shuttling between YBAP1 and YBX1?

The localization of miR223mut has not been tested in our current study. We plan to conduct these experiments in the future.

9) Supplement 3c - Is it strange that miR190 is not localized to any particular compartment? Is miR190 present ubiquitously and equally among all intracellular compartments?

Most mature miRNAs are predominantly localized in the cytoplasm. Although there is no specific subcellular localization reported for miR190 in the literature, our experimental findings indicate a relatively high expression of miR190 in 293T cells. It is likely that most of miR190 is localized in the cytosol. However, it is also possible that a small fraction of miR190 may associate with a membrane, which could explain its distribution in various subcellular structures. Importantly, we did not observe enrichment of miR190 in the mitochondria or exosomes.

10) Figure 3h - Why would the miR223 levels increase if you remove mitochondria? Does CCCP also cause miR223 upregulation? I would have thought miR223 would just be mis-localized to the cytosol.

We report that the levels of cytoplasmic miR223 increase following the removal of mitochondria using CCCP treatment. While we cannot rule out the possibility that upregulation of miR223 is directly caused by CCCP treatment, we suggest that miR223 becomes mis-localized to the cytosol upon mitochondrial removal. Our data suggests that mitochondria contribute to the secretion of miR223 into exosomes. When mitochondria are removed by mitophagy, cytosolic miR223 is not efficiently secreted, which provides an alternative explanation for the observed increase in miR223 level after mitochondrial removal.

11) Figure 3i - What is the meaning of "Urd" in the figure label? This isn't mentioned anywhere.

“Urd” represents Uridine. Uridine is now spelled out in figure 3i. The absence of mitochondria can impact the function of the mitochondrial enzyme dihydroorotate dehydrogenase, which plays a role in pyrimidine synthesis. To address this issue, one approach is to supplement the cell culture medium with Urd. A previous study demonstrated that primary fibroblasts showed positive responses when Urd was added to the cell culture medium, resulting in improved cell viability for extended periods of time (Correia-Melo et al., 2017).

12) Figure 3j - The data is presented as a ratio of EV/cell. Again, this inaccurately represents the amount of miR223 in the EV. This issue is apparent when looking at Figures 3h and 3j. In 3h, CCCP causes an upregulation of intracellular miR223. As such, the presumed decrease in EV miR233 after CCCP (3j) could be an artifact due to increased levels of intracellular miR223. Both intracellular and EV levels of miRs need to be shown.

Both the intracellular and exosomal levels of miR223 have been included in Figure 3j.

13) In Figure 4, the authors show that when overexpressed, YBX1 will pulldown YBAP1. Can the authors comment as to why none of the earlier purifications show this finding (Figure 1 for example)? Even more curious is that when YBAP1 is purified, YBX1 does not co-purify (Figure 4 supplement 1a, b).

In Figure 4a-b, human YBX1 fused with a Strep II tag was purified from 293T cells using Strep-Tactin® Sepharose® resin in a one-step purification process. Our data has shown that YBAP1 is expressed in 293T cells.

In Figure 1 and Figure 4 Supplement 1a, human YBX1 or YBAP1 fused with His and MBP tags were purified from insect cells using a three-step purification process involving Ni-NTA His-Pur resin, amylose resin, and Superdex-200 gel filtration chromatography.

One possibility is that human YBX1 or YBAP1 may not interact well with insect YBAP1 or YBX1, which could result in separate tagged forms of YBX1 or YBAP1 isolated from insect cells.

Another possibility is that the expression levels of insect YBAP1 and YBX1 may be too low. Consequently, tagged forms YBX1 or YBAP1 expressed in insect cells may copurify with partners not readily detected by Coomassie blue stain. However, in Figure 4 Supplement 1b, human YBX1 fused with His and MBP tags was co-expressed with non-tagged human YBAP1, and both bands of YBX1 and YBAP1 were visible on the Coomassie blue gel after purification using Ni-NTA His-Pur resin, amylose resin, and Superdex-200 gel filtration chromatography.

14) Figure 4f, g - The text associated with these figures is very confusing, as is the labeling for the input. Also, what is "miR223 Fold change" in this regard? Seeing as your IgG should not have IP'd anything, normalizing to IgG can amplify noise. As such, RIP assays are typically presented as % input or fold enrichment.

The RIP assay results have been calculated and presented as a % input in Figure 4g.

15) Figure 4h - The authors show binding between miR223 and YBAP1 however it is not clear how significant this binding is. There is more than a 30-fold difference in binding affinity between miR223 and YBX1 than between miR223 and YBAP1. Even more, when comparing the EMSAs and fraction bound from figures 1 and 2 to those of Figure 4h, the binding between miR223 and YBAP1 more closely resembles that of miR190 and YBX1, which the authors state is a non-binder of YBX1. The authors will need to reconcile these discrepancies.

We agree that the binding of YBAP and YBX1 differ quite significantly in the affinity of their interaction with miR223. It is difficult to draw conclusions from a comparison of the affinities of YBX1 for miR190 and YBAP1 for miR223. Nonetheless, a quantitative difference in the interaction of YBAP1 with miR223 and miR190 is apparent (Fig. 4 h, I, j) and we observed no enrichment miR190 in isolated mitochondria (Fig. 3 supplement 1a) whereas YBAP1 selectively IP’d miR223 from isolated mitochondria (Fig. 4 f and g).

16) Can the authors present the Kd values for EMSA data?

The Kd values for the EMSA data have been added to the respective figures.

17) Figure 5 - Does YBAP1-KO affect mitochondrial protein integrity or numbers?

We generated stable cell lines expressing 3xHA-GFP-OMP25 in both 293T WT and YBAP1-KO cells, but we did not observe any alterations in mitochondrial morphology (Author response image 1).

Author response image 1.

Additionally, we performed a comparison of different mitochondrial markers using immunoblot in 293T WT cells and YBAP1-KO cells and did not observe any changes in these markers (data has been included in Figure 5b.).

18) Figure 6a - Are the authors using YBAP1 as their mitochondrial marker? Please include TOM20 and/or 22.

In Figure 4c and 4e, our data clearly demonstrate that the majority of YBAP1 is localized in the mitochondria.

To further validate this localization, we performed immunofluorescence staining using antibodies against endogenous Tom20 and YBX1. The immunofluorescence images document YBX1 associated with mitochondria (Author response image 2 and new Fig 6a.).

Author response image 2.

19) Figure 6b - Rab5 is an early endosome marker and may not fully represent the organelles that become MVBs. Co-localization at this point does not suggest that associating proteins will be present in the exosome, and it is possible that the authors are looking at the precursor of a recycling endosome. Even more, exosome loading does not occur at the early endosome, but instead at the MVB. Perhaps looking at markers of the late endosome such as Rab7 or ideally markers of the MVB such as M6P or CD63 would help draw an association between YBX1, YBAP1, and the exosome. Also, If the authors want to make the claim that interactions at the early endosome leads to secretion as an exosome, the authors should show that isolated EVs from Rab5Q79L-expressing cells contain miR223.

We have previously used overexpressed Rab5(Q79L) to monitor the localization of exosomal content, specifically CD63 and YBX1, in enlarged endosomes (Liu et al. 2021, Fig. 4A, B). These endosomes exhibit a mixture of early and late endocytic markers, including CD63. (Wegner et al., 2010). Hence, the presence of Rab5(Q79L)-positive enlarged endosomes does not solely indicate early endosomes.

20) The mentioning of P-bodies is interesting but at no time is an association addressed. This is therefore an overly speculative conclusion. Either show an association or leave this out of the manuscript.

In a previous paper we demonstrated that YBX1 puncta colocalize with P-body markers EDC4, Dcp1 and DDX6 (Liu et al., 2021).

21) In lines 55-58, the authors make the comment "However, many of these studies used sedimentation at ~100,000 g to collect EVs, which may also collect RNP particles not enclosed within membranes which complicates the interpretation of these data." Do RNPs not dissolve when secreted? Can the authors give a reference for this statement?

In a previous paper, we demonstrated that the RNP Ago2 does not dissolve in the conditioned medium and is not in vesicles but sediments to the bottom of a density gradient (Temoche-Diaz et al., 2019).

Author response:

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

Reviewer #1 (Public Review):

Strengths:

The study was designed as a 6-month follow-up, with repeated behavioral and EEG measurements through disease development, providing valuable and interesting findings on AD progression and the effect of early-life choline supplantation. Moreover, the behavioral data that suggest an adverse effect of low choline in WT mice are interesting and important beyond the context of AD.

Thank you for identifying several strengths.

Weaknesses:

(1) The multiple headings and subheadings, focusing on the experimental method rather than the narrative, reduce the readability.

We have reduced the number of headings.

(2) Quantification of NeuN and FosB in WT littermates is needed to demonstrate rescue of neuronal death and hyperexcitability by high choline supplementation and also to gain further insights into the adverse effect of low choline on the performance of WT mice in the behavioral test.

We agree and have added WT data for the NeuN and ΔFosB analyses. These data are included in the text and figures. For NeuN, the Figure is Figure 6. For ΔFosB it is Figure 7. In brief, the high choline diet restored NeuN and ΔFosB to the levels of WT mice.

Below is Figure 6 and its legend to show the revised presentation of data for NeuN. Afterwards is the revised figure showing data for ΔFosB. After that are the sections of the Results that have been revised.

Author response image 1.

Choline supplementation improved NeuN immunoreactivity (ir) in hilar cells in Tg2576 animals. A. Representative images of NeuN-ir staining in the anterior DG of Tg2576 animals. (1) A section from a Tg2576 mouse fed the low choline diet. The area surrounded by a box is expanded below. Red arrows point to NeuN-ir hilar cells. Mol=molecular layer, GCL=granule cell layer, HIL=hilus. Calibration for the top row, 100 µm; for the bottom row, 50 µm. (2) A section from a Tg2576 mouse fed the intermediate diet. Same calibrations as for 1. (3) A section from a Tg2576 mouse fed the high choline diet. Same calibrations as for 1. B. Quantification methods. Representative images demonstrate the thresholding criteria used to quantify NeuN-ir. (1) A NeuN-stained section. The area surrounded by the white box is expanded in the inset (arrow) to show 3 hilar cells. The 2 NeuN-ir cells above threshold are marked by blue arrows. The 1 NeuN-ir cell below threshold is marked by a green arrow. (2) After converting the image to grayscale, the cells above threshold were designated as red. The inset shows that the two cells that were marked by blue arrows are red while the cell below threshold is not. (3) An example of the threshold menu from ImageJ showing the way the threshold was set. Sliders (red circles) were used to move the threshold to the left or right of the histogram of intensity values. The final position of the slider (red arrow) was positioned at the onset of the steep rise of the histogram. C. NeuN-ir in Tg2576 and WT mice. Tg2576 mice had either the low, intermediate, or high choline diet in early life. WT mice were fed the standard diet (intermediate choline). (1) Tg2576 mice treated with the high choline diet had significantly more hilar NeuN-ir cells in the anterior DG compared to Tg2576 mice that had been fed the low choline or intermediate diet. The values for Tg2576 mice that received the high choline diet were not significantly different from WT mice, suggesting that the high choline diet restored NeuN-ir. (2) There was no effect of diet or genotype in the posterior DG, probably because the low choline and intermediate diet did not appear to lower hilar NeuN-ir.

Author response image 2.

Choline supplementation reduced ∆FosB expression in dorsal GCs of Tg2576 mice. A. Representative images of ∆FosB staining in GCL of Tg2576 animals from each treatment group. (1) A section from a low choline-treated mouse shows robust ∆FosB-ir in the GCL. Calibration, 100 µm. Sections from intermediate (2) and high choline (3)-treated mice. Same calibration as 1. B. Quantification methods. Representative images demonstrating the thresholding criteria established to quantify ∆FosB. (1) A ∆FosB -stained section shows strongly-stained cells (white arrows). (2) A strict thresholding criteria was used to make only the darkest stained cells red. C. Use of the strict threshold to quantify ∆FosB-ir. (1) Anterior DG. Tg2576 mice treated with the choline supplemented diet had significantly less ∆FosB-ir compared to the Tg2576 mice fed the low or intermediate diets. Tg2576 mice fed the high choline diet were not significantly different from WT mice, suggesting a rescue of ∆FosB-ir. (2) There were no significant differences in ∆FosB-ir in posterior sections. D. Methods are shown using a threshold that was less strict. (1) Some of the stained cells that were included are not as dark as those used for the strict threshold (white arrows). (2) All cells above the less conservative threshold are shown in red. E. Use of the less strict threshold to quantify ∆FosB-ir. (1) Anterior DG. Tg2576 mice that were fed the high choline diet had less ΔFosB-ir pixels than the mice that were fed the other diets. There were no differences from WT mice, suggesting restoration of ∆FosB-ir by choline enrichment in early life. (2) Posterior DG. There were no significant differences between Tg2576 mice fed the 3 diets or WT mice.

Results, Section C1, starting on Line 691:

“To ask if the improvement in NeuN after MCS in Tg256 restored NeuN to WT levels we used WT mice. For this analysis we used a one-way ANOVA with 4 groups: Low choline Tg2576, Intermediate Tg2576, High choline Tg2576, and Intermediate WT (Figure 5C). Tukey-Kramer multiple comparisons tests were used as the post hoc tests. The WT mice were fed the intermediate diet because it is the standard mouse chow, and this group was intended to reflect normal mice. The results showed a significant group difference for anterior DG (F(3,25)=9.20; p=0.0003; Figure 5C1) but not posterior DG (F(3,28)=0.867; p=0.450; Figure 5C2). Regarding the anterior DG, there were more NeuN-ir cells in high choline-treated mice than both low choline (p=0.046) and intermediate choline-treated Tg2576 mice (p=0.003). WT mice had more NeuN-ir cells than Tg2576 mice fed the low (p=0.011) or intermediate diet (p=0.003). Tg2576 mice that were fed the high choline diet were not significantly different from WT (p=0.827).”

Results, Section C2, starting on Line 722:

“There was strong expression of ∆FosB in Tg2576 GCs in mice fed the low choline diet (Figure 7A1). The high choline diet and intermediate diet appeared to show less GCL ΔFosB-ir (Figure 7A2-3). A two-way ANOVA was conducted with the experimental group (Tg2576 low choline diet, Tg2576 intermediate choline diet, Tg2576 high choline diet, WT intermediate choline diet) and location (anterior or posterior) as main factors. There was a significant effect of group (F(3,32)=13.80, p=<0.0001) and location (F(1,32)=8.69, p=0.006). Tukey-Kramer post-hoc tests showed that Tg2576 mice fed the low choline diet had significantly greater ΔFosB-ir than Tg2576 mice fed the high choline diet (p=0.0005) and WT mice (p=0.0007). Tg2576 mice fed the low and intermediate diets were not significantly different (p=0.275). Tg2576 mice fed the high choline diet were not significantly different from WT (p>0.999). There were no differences between groups for the posterior DG (all p>0.05).”

“∆FosB quantification was repeated with a lower threshold to define ∆FosB-ir GCs (see Methods) and results were the same (Figure 7D). Two-way ANOVA showed a significant effect of group (F(3,32)=14.28, p< 0.0001) and location (F(1,32)=7.07, p=0.0122) for anterior DG but not posterior DG (Figure 7D). For anterior sections, Tukey-Kramer post hoc tests showed that low choline mice had greater ΔFosB-ir than high choline mice (p=0.0024) and WT mice (p=0.005) but not Tg2576 mice fed the intermediate diet (p=0.275); Figure 7D1). Mice fed the high choline diet were not significantly different from WT (p=0.993; Figure 7D1). These data suggest that high choline in the diet early in life can reduce neuronal activity of GCs in offspring later in life. In addition, low choline has an opposite effect, suggesting low choline in early life has adverse effects.”

(3) Quantification of the discrimination ratio of the novel object and novel location tests can facilitate the comparison between the different genotypes and diets.

We have added the discrimination index for novel object location to the paper. The data are in a new figure: Figure 3. In brief, the results for discrimination index are the same as the results done originally, based on the analysis of percent of time exploring the novel object.

Below is the new Figure and legend, followed by the new text in the Results.

Author response image 3.

Novel object location results based on the discrimination index. A. Results are shown for the 3 months-old WT and Tg2576 mice based on the discrimination index. (1) Mice fed the low choline diet showed object location memory only in WT. (2) Mice fed the intermediate diet showed object location memory only in WT. (3) Mice fed the high choline diet showed memory both for WT and Tg2576 mice. Therefore, the high choline diet improved memory in Tg2576 mice. B. The results for the 6 months-old mice are shown. (1-2) There was no significant memory demonstrated by mice that were fed either the low or intermediate choline diet. (3) Mice fed a diet enriched in choline showed memory whether they were WT or Tg2576 mice. Therefore, choline enrichment improved memory in all mice.

Results, Section B1, starting on line 536:

“The discrimination indices are shown in Figure 3 and results led to the same conclusions as the analyses in Figure 2. For the 3 months-old mice (Figure 3A), the low choline group did not show the ability to perform the task for WT or Tg2576 mice. Thus, a two-way ANOVA showed no effect of genotype (F(1,74)=0.027, p=0.870) or task phase (F(1,74)=1.41, p=0.239). For the intermediate diet-treated mice, there was no effect of genotype (F(1,50)=0.3.52, p=0.067) but there was an effect of task phase (F(1,50)=8.33, p=0.006). WT mice showed a greater discrimination index during testing relative to training (p=0.019) but Tg2576 mice did not (p=0.664). Therefore, Tg2576 mice fed the intermediate diet were impaired. In contrast, high choline-treated mice performed well. There was a main effect of task phase (F(1,68)=39.61, p=<0.001) with WT (p<0.0001) and Tg2576 mice (p=0.0002) showing preference for the moved object in the test phase. Interestingly, there was a main effect of genotype (F(1,68)=4.50, p=0.038) because the discrimination index for WT training was significantly different from Tg2576 testing (p<0.0001) and Tg2576 training was significantly different from WT testing (p=0.0003).”

“The discrimination indices of 6 months-old mice led to the same conclusions as the results in Figure 2. There was no evidence of discrimination in low choline-treated mice by two-way ANOVA (no effect of genotype, (F(1,42)=3.25, p=0.079; no effect of task phase, F(1,42)=0.278, p=0.601). The same was true of mice fed the intermediate diet (genotype, F(1,12)=1.44, p=0.253; task phase, F(1,12)=2.64, p=0.130). However, both WT and Tg2576 mice performed well after being fed the high choline diet (effect of task phase, (F(1,52)=58.75, p=0.0001, but not genotype (F(1,52)=1.197, p=0.279). Tukey-Kramer post-hoc tests showed that both WT (p<0.0001) and Tg2576 mice that had received the high choline diet (p=0.0005) had elevated discrimination indices for the test session.”

(4) The longitudinal analyses enable the performance of multi-level correlations between the discrimination ratio in NOR and NOL, NeuN and Fos levels, multiple EEG parameters, and premature death. Such analysis can potentially identify biomarkers associated with AD progression. These can be interesting in different choline supplementation, but also in the standard choline diet.

We agree and added correlations to the paper in a new figure (Figure 9). Below is Figure 9 and its legend. Afterwards is the new Results section.

Author response image 4.

Correlations between IIS, Behavior, and hilar NeuN-ir. A. IIS frequency over 24 hrs is plotted against the preference for the novel object in the test phase of NOL. A greater preference is reflected by a greater percentage of time exploring the novel object. (1) The mice fed the high choline diet (red) showed greater preference for the novel object when IIS were low. These data suggest IIS impaired object location memory in the high choline-treated mice. The low choline-treated mice had very weak preference and very few IIS, potentially explaining the lack of correlation in these mice. (2) There were no significant correlations for IIS and NOR. However, there were only 4 mice for the high choline group, which is a limitation. B. IIS frequency over 24 hrs is plotted against the number of dorsal hilar cells expressing NeuN. The dorsal hilus was used because there was no effect of diet on the posterior hilus. (1) Hilar NeuN-ir is plotted against the preference for the novel object in the test phase of NOL. There were no significant correlations. (2) Hilar NeuN-ir was greater for mice that had better performance in NOR, both for the low choline (blue) and high choline (red) groups. These data support the idea that hilar cells contribute to object recognition (Kesner et al. 2015; Botterill et al. 2021; GoodSmith et al. 2022).

Results, Section F, starting on Line 801:

“F. Correlations between IIS and other measurements

As shown in Figure 9A, IIS were correlated to behavioral performance in some conditions. For these correlations, only mice that were fed the low and high choline diets were included because mice that were fed the intermediate diet did not have sufficient EEG recordings in the same mouse where behavior was studied. IIS frequency over 24 hrs was plotted against the preference for the novel object in the test phase (Figure 9A). For NOL, IIS were significantly less frequent when behavior was the best, but only for the high choline-treated mice (Pearson’s r, p=0.022). In the low choline group, behavioral performance was poor regardless of IIS frequency (Pearson’s r, p=0.933; Figure 9A1). For NOR, there were no significant correlations (low choliNe, p=0.202; high choline, p=0.680) but few mice were tested in the high choline-treated mice (Figure 9B2).

We also tested whether there were correlations between dorsal hilar NeuN-ir cell numbers and IIS frequency. In Figure 9B, IIS frequency over 24 hrs was plotted against the number of dorsal hilar cells expressing NeuN. The dorsal hilus was used because there was no effect of diet on the posterior hilus. For NOL, there was no significant correlation (low choline, p=0.273; high choline, p=0.159; Figure 9B1). However, for NOR, there were more NeuN-ir hilar cells when the behavioral performance was strongest (low choline, p=0.024; high choline, p=0.016; Figure 9B2). These data support prior studies showing that hilar cells, especially mossy cells (the majority of hilar neurons), contribute to object recognition (Botterill et al. 2021; GoodSmith et al. 2022).”

We also noted that all mice were not possible to include because they died or other reasons, such a a loss of the headset (Results, Section A, Lines 463-464): Some mice were not possible to include in all assays either because they died before reaching 6 months or for other reasons.

Reviewer #2 (Public Review):

Strengths:

The strength of the group was the ability to monitor the incidence of interictal spikes (IIS) over the course of 1.2-6 months in the Tg2576 Alzheimer's disease model, combined with meaningful behavioral and histological measures. The authors were able to demonstrate MCS had protective effects in Tg2576 mice, which was particularly convincing in the hippocampal novel object location task.

We thank the Reviewer for identifying several strengths.

Weaknesses:

Although choline deficiency was associated with impaired learning and elevated FosB expression, consistent with increased hyperexcitability, IIS was reduced with both low and high choline diets. Although not necessarily a weakness, it complicates the interpretation and requires further evaluation.

We agree and we revised the paper to address the evaluations that were suggested.

Reviewer #1 (Recommendations For The Authors):

(1) A reference directing to genotyping of Tg2576 mice is missing.

We apologize for the oversight and added that the mice were genotyped by the New York University Mouse Genotyping core facility.

Methods, Section A, Lines 210-211: “Genotypes were determined by the New York University Mouse Genotyping Core facility using a protocol to detect APP695.”

(2) Which software was used to track the mice in the behavioral tests?

We manually reviewed videos. This has been clarified in the revised manuscript. Methods, Section B4, Lines 268-270: Videos of the training and testing sessions were analyzed manually. A subset of data was analyzed by two independent blinded investigators and they were in agreement.

(3) Unexpectedly, a low choline diet in AD mice was associated with reduced frequency of interictal spikes yet increased mortality and spontaneous seizures. The authors attribute this to postictal suppression.

We did not intend to suggest that postictal depression was the only cause. It was a suggestion for one of many potential explanations why seizures would influence IIS frequency. For postictal depression, we suggested that postictal depression could transiently reduce IIS. We have clarified the text so this is clear (Discussion, starting on Line 960):

If mice were unhealthy, IIS might have been reduced due to impaired excitatory synaptic function. Another reason for reduced IIS is that the mice that had the low choline diet had seizures which interrupted REM sleep. Thus, seizures in Tg2576 mice typically started in sleep. Less REM sleep would reduce IIS because IIS occur primarily in REM. Also, seizures in the Tg2576 mice were followed by a depression of the EEG (postictal depression; Supplemental Figure 3) that would transiently reduce IIS. A different, radical explanation is that the intermediate diet promoted IIS rather than low choline reducing IIS. Instead of choline, a constituent of the intermediate diet may have promoted IIS.

However, reduced spike frequency is already evident at 5 weeks of age, a time point with a low occurrence of premature death. A more comprehensive analysis of EEG background activity may provide additional information if the epileptic activity is indeed reduced at this age.

We did not intend to suggest that premature death caused reduced spike frequency. We have clarified the paper accordingly. We agree that a more in-depth EEG analysis would be useful but is beyond the scope of the study.

(4) Supplementary Fig. 3 depicts far more spikes / 24 h compared to Fig. 7B (at least 100 spikes/24h in Supplementary Fig. 3 and less than 10 spikes/24h in Fig. 7B).

We would like to clarify that before and after a seizure the spike frequency is unusually high. Therefore, there are far more spikes than prior figures.

We clarified this issue by adding to the Supplemental Figure more data. The additional data are from mice without a seizure, showing their spikes are low in frequency.

All recordings lasted several days. We included the data from mice with a seizure on one of the days and mice without any seizures. For mice with a seizure, we graphed IIS frequency for the day before, the day of the seizure, and the day after. For mice without a seizure, IIS frequency is plotted for 3 consecutive days. When there was a seizure, the day before and after showed high numbers of spikes. When there was no seizure on any of the 3 days, spikes were infrequent on all days.

The revised figure and legend are shown below. It is Supplemental Figure 4 in the revised submission.

Author response image 5.

IIS frequency before and after seizures. A. Representative EEG traces recorded from electrodes implanted in the skull over the left frontal cortex, right occipital cortex, left hippocampus (Hippo) and right hippocampus during a spontaneous seizure in a 5 months-old Tg2576 mouse. Arrows point to the start (green arrow) and end of the seizure (red arrow), and postictal depression (blue arrow). B. IIS frequency was quantified from continuous video-EEG for mice that had a spontaneous seizure during the recording period and mice that did not. IIS frequency is plotted for 3 consecutive days, starting with the day before the seizure (designated as day 1), and ending with the day after the seizure (day 3). A two-way RMANOVA was conducted with the day and group (mice with or without a seizure) as main factors. There was a significant effect of day (F(2,4)=46.95, p=0.002) and group (seizure vs no seizure; F(1,2)=46.01, p=0.021) and an interaction of factors (F(2,4)=46.68, p=0.002)..Tukey-Kramer post-hoc tests showed that mice with a seizure had significantly greater IIS frequencies than mice without a seizure for every day (day 1, p=0.0005; day 2, p=0.0001; day 3, p=0.0014). For mice with a seizure, IIS frequency was higher on the day of the seizure than the day before (p=0.037) or after (p=0.010). For mice without a seizure, there were no significant differences in IIS frequency for day 1, 2, or 3. These data are similar to prior work showing that from one day to the next mice without seizures have similar IIS frequencies (Kam et al., 2016).

In the text, the revised section is in the Results, Section C, starting on Line 772:

“At 5-6 months, IIS frequencies were not significantly different in the mice fed the different diets (all p>0.05), probably because IIS frequency becomes increasingly variable with age (Kam et al. 2016). One source of variability is seizures, because there was a sharp increase in IIS during the day before and after a seizure (Supplemental Figure 4). Another reason that the diets failed to show differences was that the IIS frequency generally declined at 5-6 months. This can be appreciated in Figure 8B and Supplemental Figure 6B. These data are consistent with prior studies of Tg2576 mice where IIS increased from 1 to 3 months but then waxed and waned afterwards (Kam et al., 2016).”

(5) The data indicating the protective effect of high choline supplementation are valuable, yet some of the claims are not completely supported by the data, mainly as the analysis of littermate WT mice is not complete.

We added WT data to show that the high choline diet restored cell loss and ΔFosB expression to WT levels. These data strengthen the argument that the high choline diet was valuable. See the response to Reviewer #1, Public Review Point #2.

• Line 591: "The results suggest that choline enrichment protected hilar neurons from NeuN loss in Tg2576 mice." A comparison to NeuN expression in WT mice is needed to make this statement.

These data have been added. See the response to Reviewer #1, Public Review Point #2.

• Line 623: "These data suggest that high choline in the diet early in life can reduce hyperexcitability of GCs in offspring later in life. In addition, low choline has an opposite effect, again suggesting this maternal diet has adverse effects." Also here, FosB quantification in WT mice is needed.

These data have been added. See the response to Reviewer #1, Public Review Point #2.

(7) Was the effect of choline associated with reduced tauopathy or A levels?

The mice have no detectable hyperphosphorylated tau. The mice do have intracellular A before 6 months. This is especially the case in hilar neurons, but GCs have little (Criscuolo et al., eNeuro, 2023). However, in neurons that have reduced NeuN, we found previously that antibodies generally do not work well. We think it is because the neurons become pyknotic (Duffy et al., 2015), a condition associated with oxidative stress which causes antigens like NeuN to change conformation due to phosphorylation. Therefore, we did not conduct a comparison of hilar neurons across the different diets.

(8) Since the mice were tested at 3 months and 6 months, it would be interesting to see the behavioral difference per mouse and the correlation with EEG recording and immunohistological analyses.

We agree that would be valuable and this has been added to the paper. Please see response to Reviewer #1, Public Review Point #4.

Reviewer #2 (Recommendations For The Authors):

There were several areas that could be further improved, particularly in the areas of data analysis (particularly with images and supplemental figures), figure presentation, and mechanistic speculation.

Major points:

(1) It is understandable that, for the sake of labor and expense, WT mice were not implanted with EEG electrodes, particularly since previous work showed that WT mice have no IIS (Kam et al. 2016). However, from a standpoint of full factorial experimental design, there are several flaws - purists would argue are fatal flaws. First, the lack of WT groups creates underpowered and imbalanced groups, constraining statistical comparisons and likely reducing the significance of the results. Also, it is an assumption that diet does not influence IIS in WT mice. Secondly, with a within-subject experimental design (as described in Fig. 1A), 6-month-old mice are not naïve if they have previously been tested at 3 months. Such an experimental design may reduce effect size compared to non-naïve mice. These caveats should be included in the Discussion. It is likely that these caveats reduce effect size and that the actual statistical significance, were the experimental design perfect, would be higher overall.

We agree and have added these points to the Limitations section of the Discussion. Starting on Line 1050: In addition, groups were not exactly matched. Although WT mice do not have IIS, a WT group for each of the Tg2576 groups would have been useful. Instead, we included WT mice for the behavioral tasks and some of the anatomical assays. Related to this point is that several mice died during the long-term EEG monitoring of IIS.

(2) Since behavior, EEG, NeuN and FosB experiments seem to be done on every Tg2576 animal, it seems that there are missed opportunities to correlate behavior/EEG and histology on a per-mouse basis. For example, rather than speculate in the discussion, why not (for example) directly examine relationships between IIS/24 hours and FosB expression?

We addressed this point above in responding to Reviewer #1, Public Review Point #4.

(3) Methods of image quantification should be improved. Background subtraction should be considered in the analysis workflow (see Fig. 5C and Fig. 6C background). It would be helpful to have a Methods figure illustrating intermediate processing steps for both NeuN and FosB expression.

We added more information to improve the methods of quantification. We did use a background subtraction approach where ImageJ provides a histogram of intensity values, and it determines when there is a sharp rise in staining relative to background. That point is where we set threshold. We think it is a procedure that has the least subjectivity.

We added these methods to the Methods section and expanded the first figure about image quantification, Figure 6B. That figure and legend are shown above in response to Reviewer #1, Point #2.

This is the revised section of the Methods, Section C3, starting on Line 345:

“Photomicrographs were acquired using ImagePro Plus V7.0 (Media Cybernetics) and a digital camera (Model RET 2000R-F-CLR-12, Q-Imaging). NeuN and ∆FosB staining were quantified from micrographs using ImageJ (V1.44, National Institutes of Health). All images were first converted to grayscale and in each section, the hilus was traced, defined by zone 4 of Amaral (1978). A threshold was then calculated to identify the NeuN-stained cell bodies but not background. Then NeuN-stained cell bodies in the hilus were quantified manually. Note that the threshold was defined in ImageJ using the distribution of intensities in the micrograph. A threshold was then set using a slider in the histogram provided by Image J. The slider was pushed from the low level of staining (similar to background) to the location where staining intensity made a sharp rise, reflecting stained cells. Cells with labeling that was above threshold were counted.”

(4) This reviewer is surprised that the authors do not speculate more about ACh-related mechanisms. For example, choline deficiency would likely reduce Ach release, which could have the same effect on IIS as muscarinic antagonism (Kam et al. 2016), and could potentially explain the paradoxical effects of a low choline diet on reducing IIS. Some additional mechanistic speculation would be helpful in the Discussion.

We thank the Reviewer for noting this so we could add it to the Discussion. We had not because we were concerned about space limitations.

The Discussion has a new section starting on Line 1009:

“Choline and cholinergic neurons

There are many suggestions for the mechanisms that allow MCS to improve health of the offspring. One hypothesis that we are interested in is that MCS improves outcomes by reducing IIS. Reducing IIS would potentially reduce hyperactivity, which is significant because hyperactivity can increase release of A. IIS would also be likely to disrupt sleep since it represents aberrant synchronous activity over widespread brain regions. The disruption to sleep could impair memory consolidation, since it is a notable function of sleep (Graves et al. 2001; Poe et al. 2010). Sleep disruption also has other negative consequences such as impairing normal clearance of A (Nedergaard and Goldman 2020). In patients, IIS and similar events, IEDs, are correlated with memory impairment (Vossel et al. 2016).

How would choline supplementation in early life reduce IIS of the offspring? It may do so by making BFCNs more resilient. That is significant because BFCN abnormalities appear to cause IIS. Thus, the cholinergic antagonist atropine reduced IIS in vivo in Tg2576 mice. Selective silencing of BFCNs reduced IIS also. Atropine also reduced elevated synaptic activity of GCs in young Tg2576 mice in vitro. These studies are consistent with the idea that early in AD there is elevated cholinergic activity (DeKosky et al. 2002; Ikonomovic et al. 2003; Kelley et al. 2014; Mufson et al. 2015; Kelley et al. 2016), while later in life there is degeneration. Indeed, the chronic overactivity could cause the degeneration.

Why would MCS make BFCNs resilient? There are several possibilities that have been explored, based on genes upregulated by MCS. One attractive hypothesis is that neurotrophic support for BFCNs is retained after MCS but in aging and AD it declines (Gautier et al. 2023). The neurotrophins, notably nerve growth factor (NGF) and brain-derived neurotrophic factor (BDNF) support the health of BFCNs (Mufson et al. 2003; Niewiadomska et al. 2011).”

Minor points:

(1) The vendor is Dyets Inc., not Dyets.

Thank you. This correction has been made.

(2) Anesthesia chamber not specified (make, model, company).

We have added this information to the Methods, Section D1, starting on Line 375: The animals were anesthetized by isoflurane inhalation (3% isoflurane. 2% oxygen for induction) in a rectangular transparent plexiglas chamber (18 cm long x 10 cm wide x 8 cm high) made in-house.

(3) It is not clear whether software was used for the detection of behavior. Was position tracking software used or did blind observers individually score metrics?

We have added the information to the paper. Please see the response to Reviewer #1, Recommendations for Authors, Point #2.

(4) It is not clear why rat cages and not a true Open Field Maze were used for NOL and NOR.

We used mouse cages because in our experience that is what is ideal to detect impairments in Tg2576 mice at young ages. We think it is why we have been so successful in identifying NOL impairments in young mice. Before our work, most investigators thought behavior only became impaired later. We would like to add that, in our experience, an Open Field Maze is not the most common cage that is used.

(5) Figure 1A is not mentioned.

It had been mentioned in the Introduction. Figure B-D was the first Figure mentioned in the Results so that is why it might have been missed. We now have added it to the first section of the Results, Line 457, so it is easier to find.

6) Although Fig 7 results are somewhat complicated compared to Fig. 5 and 6 results, EEG comes chronologically earlier than NeuN and FosB expression experiments.

We have kept the order as is because as the Reviewer said, the EEG is complex. For readability, we have kept the EEG results last.

(7) Though the statistical analysis involved parametric and nonparametric tests, It is not clear which normality tests were used.

We have added the name of the normality tests in the Methods, Section E, Line 443: Tests for normality (Shapiro-Wilk) and homogeneity of variance (Bartlett’s test) were used to determine if parametric statistics could be used. We also added after this sentence clarification: When data were not normal, non-parametric data were used. When there was significant heteroscedasticity of variance, data were log transformed. If log transformation did not resolve the heteroscedasticity, non-parametric statistics were used. Because we added correlations and analysis of survival curves, we also added the following (starting on Line 451): For correlations, Pearson’s r was calculated. To compare survival curves, a Log rank (Mantel-Cox) test was performed.

Figures:

(1) In Fig. 1A, Anatomy should be placed above the line.

We changed the figure so that the word “Anatomy” is now aligned, and the arrow that was angled is no longer needed.

In Fig. 1C and 1D, the objects seem to be moved into the cage, not the mice. This schematic does not accurately reflect the Fig. 1C and 1D figure legend text.

Thank you for the excellent point. The figure has been revised. We also updated it to show the objects more accurately.

Please correct the punctuation in the Fig. 1D legend.

Thank you for mentioning the errors. We corrected the legend.

For ease of understanding, Fig. 1C and 1D should have training and testing labeled in the figure.

Thank you for the suggestion. We have revised the figure as suggested.

Author response image 6.

(2) In Figure 2, error bars for population stats (bar graphs) are not obvious or missing. Same for Figure 3.

We added two supplemental figures to show error bars, because adding the error bars to the existing figures made the symbols, colors, connecting lines and error bars hard to distinguish. For novel object location (Fig. 2) the error bars are shown in Supp. Fig. 2. For novel object recognition, the error bars are shown in Supplemental Fig. 3.

(3) The authors should consider a Methods figure for quantification of NeuN and deltaFOSB (expansions of Fig. 5C and Fig. 6C).

Please see Reviewer #1, Public Review Point #2.

(4) In Figure 5, A should be omitted and mentioned in the Methods/figure legend. B should be enlarged. C should be inset, zoomed-in images of the hilus, with an accompanying analysis image showing a clear reduction in NeuN intensity in low choline conditions compared to intermediate and high choline conditions. In D, X axes could delineate conditions (figure legend and color unnecessary). Figure 5C should be moved to a Methods figure.

We thank the review for the excellent suggestions. We removed A as suggested. We expanded B and included insets. We used different images to show a more obvious reduction of cells for the low choline group. We expanded the Methods schematics. The revised figure is Figure 6 and shown above in response to Reviewer 1, Public Review Point #2.

(5) In Figure 6, A should be eliminated and mentioned in the Methods/figure legend. B should be greatly expanded with higher and lower thresholds shown on subsequent panels (3x3 design).

We removed A as suggested. We expanded B as suggested. The higher and lower thresholds are shown in C. The revised figure is Figure 7 and shown above in response to Reviewer 1, Public Review Point #2.

(6) In Figure 7, A2 should be expanded vertically. A3 should be expanded both vertically and horizontally. B 1 and 2 should be increased, particularly B1 where it is difficult to see symbols. Perhaps colored symbols offset/staggered per group so that the spread per group is clearer.

We added a panel (A4) to show an expansion of A2 and A3. However, we did not see that a vertical expansion would add information so we opted not to add that. We expanded B1 as suggested but opted not to expand B2 because we did not think it would enhance clarity. The revised figure is below.

Author response image 7.

(7) Supplemental Figure 1 could possibly be combined with Figure 1 (use rounded corner rat cage schematic for continuity).

We opted not to combine figures because it would make one extremely large figure. As a result, the parts of the figure would be small and difficult to see.

(8) Supplemental Figure 2 - there does not seem to be any statistical analysis associated with A mentioned in the Results text.

We added the statistical information. It is now Supplemental Figure 4:

Author response image 8.

Mortality was high in mice treated with the low choline diet. A. Survival curves are shown for mice fed the low choline diet and mice fed the high choline diet. The mice fed the high choline diet had a significantly less severe survival curve. B. Left: A photo of a mouse after sudden unexplained death. The mouse was found in a posture consistent with death during a convulsive seizure. The area surrounded by the red box is expanded below to show the outstretched hindlimb (red arrow). Right: A photo of a mouse that did not die suddenly. The area surrounded by the box is expanded below to show that the hindlimb is not outstretched.

The revised text is in the Results, Section E, starting on Line 793:

“The reason that low choline-treated mice appeared to die in a seizure was that they were found in a specific posture in their cage which occurs when a severe seizure leads to death (Supplemental Figure 5). They were found in a prone posture with extended, rigid limbs (Supplemental Figure 5). Regardless of how the mice died, there was greater mortality in the low choline group compared to mice that had been fed the high choline diet (Log-rank (Mantel-Cox) test, Chi square 5.36, df 1, p=0.021; Supplemental Figure 5A).”

Also, why isn't intermediate choline also shown?

We do not have the data from the animals. Records of death were not kept, regrettably.

Perhaps labeling of male/female could also be done as part of this graph.

We agree this would be very interesting but do not have all sex information.

B is not very convincing, though it is understandable once one reads about posture.

We have clarified the text and figure, as well as the legend. They are above.

Are there additional animals that were seen to be in a specific posture?

There are many examples, and we added them to hopefully make it more convincing.

We also added posture in WT mice when there is a death to show how different it is.

Is there any relationship between seizures detected via EEG, as shown in Supplemental Figure 3, and death?

Several mice died during a convulsive seizure, which is the type of seizure that is shown in the Supplemental Figure.

(9) Supplemental Figure 3 seems to display an isolated case in which EEG-detected seizures correlate with increased IIEs. It is not clear whether there are additional documented cases of seizures that could be assembled into a meaningful population graph. If this data does not exist or is too much work to include in this manuscript, perhaps it can be saved for a future paper.

We have added other cases and revised the graph. This is now Supplemental Figure 4 and is shown above in response to Reviewer #1, Recommendation for Authors Point #4.

Frontal is misspelled.

We checked and our copy is not showing a misspelling. However, we are very grateful to the Reviewer for catching many errors and reading the manuscript carefully.

(10) Supplemental Figure 4 seems incomplete in that it does not include EEG data from months 4, 5, and 6 (see Fig. 7B).

We have added data for these ages to the Supplemental Figure (currently Supplemental Figure 6) as part B. In part A, which had been the original figure, only 1.2, 2, and 3 months-old mice were shown because there were insufficient numbers of each sex at other ages. However, by pooling 1.2 and 2 months (Supplemental Figure 6B1), 3 and 4 months (B2) and 5 and 6 months (B3) we could do the analysis of sex. The results are the same – we detected no sex differences.

Author response image 9.

A. IIS frequency was similar for each sex. A. IIS frequency was compared for females and males at 1.2 months (1), 2 months (2), and 3 months (3). Two-way ANOVA was used to analyze the effects of sex and diet. Female and male Tg2576 mice were not significantly different. B. Mice were pooled at 1.2 and 2 months (1), 3 and 4 months (2) and 5 and 6 months (3). Two-way ANOVA analyzed the effects of sex and diet. There were significant effects of diet for (1) and (2) but not (3). There were no effects of sex at any age. (1) There were significant effects of diet (F(2,47)=46.21, p<0.0001) but not sex (F(1,47)=0.106, p=0.746). Female and male mice fed the low choline diet or high choline diet were significantly different from female and male mice fed the intermediate diet (all p<0.05, asterisk). (2) There were significant effects of diet (F(2,32)=10.82, p=0.0003) but not sex (F(1,32)=1.05, p=0.313). Both female and male mice of the low choline group were significantly different from male mice fed the intermediate diet (both p<0.05, asterisk) but no other pairwise comparisons were significant. (3) There were no significant differences (diet, F(2,23)=1.21, p=0.317); sex, F(1,23)=0.844, p=0.368).

The data are discussed the Results, Section G, tarting on Line 843:

In Supplemental Figure 6B we grouped mice at 1-2 months, 3-4 months and 5-6 months so that there were sufficient females and males to compare each diet. A two-way ANOVA with diet and sex as factors showed a significant effect of diet (F(2,47)=46.21; p<0.0001) at 1-2 months of age, but not sex (F1,47)=0.11, p=0.758). Post-hoc comparisons showed that the low choline group had fewer IIS than the intermediate group, and the same was true for the high choline-treated mice. Thus, female mice fed the low choline diet differed from the females (p<0.0001) and males (p<0.0001) fed the intermediate diet. Male mice that had received the low choline diet different from females (p<0.0001) and males (p<0.0001) fed the intermediate diet. Female mice fed the high choline diet different from females (p=0.002) and males (p<0.0001) fed the intermediate diet, and males fed the high choline diet difference from females (p<0.0001) and males (p<0.0001) fed the intermediate diet.

For the 3-4 months-old mice there was also a significant effect of diet (F(2,32)=10.82, p=0.0003) but not sex (F(1,32)=1.05, p=0.313). Post-hoc tests showed that low choline females were different from males fed the intermediate diet (p=0.007), and low choline males were also significantly different from males that had received the intermediate diet (p=0.006). There were no significant effects of diet (F(2,23)=1.21, p=0.317) or sex (F(1,23)=0.84, p=0.368) at 5-6 months of age.

Author Response

Reviewer #1 (Public Review):

Weaknesses:

Gene expression level as a confounding factor was not well controlled throughout the study. Higher gene expression often makes genes less dispensable after gene duplication. Gene expression level is also a major determining factor of evolutionary rates (reviewed in http://www.ncbi.nlm.nih.gov/pubmed/26055156). Some proposed theories explain why gene expression level can serve as a proxy for gene importance (http://www.ncbi.nlm.nih.gov/pubmed/20884723, http://www.ncbi.nlm.nih.gov/pubmed/20485561). In that sense, many genomic/epigenomic features (such as replication timing and repressed transcriptional regulation) that were assumed "neutral" or intrinsic by the authors (or more accurately, independent of gene dispensability) cannot be easily distinguishable from the effect of gene dispersibility.

We thank the reviewer for this important comment. We totally agree that transcriptomic and epigenomic features cannot be easily distinguished from gene dispensability and do not think that these features of the elusive genes can be explained solely by intrinsic properties of the genomes. Our motivation for investigating the expression profiles of the elusive gene is to understand how they lost their functional indispensability (original manuscript L285-286 in Results). We also discussed the possibility that sequence composition and genomic location of elusive genes may be associated with epigenetic features for expression depression, which may result in a decrease of functional constraints (original manuscript L470-474 in Discussion). Nevertheless, we think that the original manuscript may have contained misleading wordings, and thus we have edited them to better convey our view that gene expression and epigenomic features are related to gene function.

(P.2, Introduction) This evolutionary fate of a gene can also be affected by factors independent of gene dispensability, including the mutability of genomic positions, but such features have not been examined well.

(P6, Introduction) These data assisted us to understand how intrinsic genomic features may affect gene fate, leading to gene loss by decreasing the expression level and eventually relaxing the functional importance of ʻelusiveʼ genes.

(P33, Discussion) Another factor is the spatiotemporal suppression of gene expression via epigenetic constraints. Previous studies showed that lowly expressed genes reduce their functional dispensability (Cherry, 2010; Gout et al., 2010), and so do the elusive genes.

Additionally, responding to the advices from Reviewers 1 and 2 [Rev1minor7 and Rev2-Major4], we have added a new section Elusive gene orthologs in the chicken microchromosomes in which we describe the relationship between the elusive genes and chicken microchromosomes. In this section, we also argue for the relationship between the genomic feature of the elusive genes and their transcriptomic and epigenomic characteristics. In the chicken genome, elusive genes did not show reduced pleiotropy of gene expression nor the epigenetic features relevant with the reduction, consistently with the moderation of nucleotide substitution rates. This also suggests that the relaxation of the ‘elusiveness’ is associated with the increase of functional indispensability.

(P27, Elusive gene orthologs in the chicken microchromosomes in Results) Our analyses indicates that the genomic features of the elusive genes such as high GC and high nucleotide substitutions do not always correlate with a reduction in pleiotropy of gene expression that potentially leads to an increase in functional dispensability, although these features have been well conserved across vertebrates. In addition, the avian orthologs of the elusive genes did not show higher KA and KS values than those of the non-elusive genes (Figure 3; Figure 3–figure supplement 1), likely consistent with similar expression levels between them (Figure 5–figure supplement 1) (Cherry, 2010; Zhang and Yang, 2015). With respect to the chicken genome, the sequence features of the elusive genes themselves might have been relaxed during evolution.

Ks was used by the authors to indicate mutation rates. However, synonymous mutations substantially affect gene expression levels (https://pubmed.ncbi.nlm.nih.gov/25768907/, https://pubmed.ncbi.nlm.nih.gov/35676473/). Thus, synonymous mutations cannot be simply assumed as neutral ones and may not be suitable for estimating local mutation rates. If introns can be aligned, they are better sequences for estimating the mutability of a genomic region.

We appreciate the reviewer for this meaningful suggestion. As a response, we have computed the differences in intron sequences between the human and chimpanzee genomes and compared them between the elusive and non-elusive genes. As expected, we found larger sequence differences in introns for the elusive genes than for the non-elusive genes. In Figure 2c of the revised manuscript, we have included the distribution of KI, sequence differences in introns between the human and chimpanzee genomes for the elusive and non-elusive genes. Additionally, we have added the corresponding texts to Results and the procedure to Methods as shown below.

(P11, Identification of human ‘elusive’ genes in Results) In addition, we computed nucleotide substitution rates for introns (KI) between human and chimpanzee (Pan troglodytes) orthologs and compared them between the elusive and non-elusive genes.

(P11, Identification of human ‘elusive’ genes in Results) Our analysis further illuminated larger KS and KI values for the elusive genes than in the non-elusive genes (Figure 2b, c; Figure 2–figure supplement 1). Importantly, the higher rate of synonymous and intronic nucleotide substitutions, which may not affect changes in amino acid residues, indicates that the elusive genes are also susceptible to genomic characteristics independent of selective constraints on gene functions.

(P39, Methods) To compute nucleotide sequence differences of the individual introns, we extracted 473 elusive and 4,626 non-elusive genes that harbored introns aligned with the chimpanzee genome assembly. The nucleotide differences were calculated via the whole genome alignments of hg38 and panTro6 retrieved from the UCSC genome browser.

The term "elusive gene" is not necessarily intuitive to readers.

We previously published a paper reporting the group of genes that we refer to as ‘elusive genes,’ lost in mammals and aves independently but retained by reptiles, in the gecko genome assembly (Hara et al., 2018, BMC Biology). We initially termed them with a more intuitive name (‘loss-prone genes’) but changed it because one of our peer-reviewers did not agree to use this name. Later on, we have continuously used this term in another paper (Hara et al., 2018, Nat. Ecol. Evol.). In addition, some other groups have used the word ‘elusive’ with a similar intention to ours (Prokop et al, 2014, PLOS ONE, doi: 10.1371/journal.pone.0092751; Ribas et al., 2011, BMC Genomics, doi: 10.1186/1471-2164-12-240). We would appreciate the reviewer’s understanding of this naming to ensure the consistency of our researches on gene loss. In the revised manuscript, we have added sentences to provide a more intuitive guide to ‘elusive genes’,

(P6, Introduction) We previously referred to the nature of genes prone to loss as ‘elusive’(Hara et al., 2018a, 2018b). In the present study, we define the elusive genes as those that are retained by modern humans but have been lost independently in multiple mammalian lineages. As a comparison of the elusive genes, we retrieved the genes that were retained by almost all of the mammalian species examined and defined them as ‘non-elusive’, representing those persistent in the genomes.

Reviewer #3 (Public Review):

Overall, the study is descriptive and adds incremental evidence to an existing body of extensive gene loss literature. The topic is specialised and will be of interest to a niche audience. The text is highly redundant, repeating the same false positive issue in the introduction, methods, and discussion sections, while no clear conclusion or interpretation of their main findings are presented.

Major comments

While some of the false discovery rate issues of gene loss detection were addressed in the presented pipeline, the authors fail to test one of the most severe cases of mis-annotating gene loss events: frameshift mutations which cause gene annotation pipelines to fail reporting these genes in the first place. Running a blastx or diamond blastx search of their elusive and non-elusive gene sets against all other genomes, should further enlighten the robustness of their gene loss detection approach

For the revised manuscript, we have refined the elusive gene set as the reviewer suggested. In the genome assemblies, we have searched for the orthologs of the elusive genes for the species in which they were missing. The search has been conducted by querying amino acid sequences of the elusive genes with tblastn as well as MMSeqs2 that performed superior to tblastn in sensitivity and computational speed. In addition, regarding another comment by Reviewer 3. we have searched for the orthologs by referring to existing ortholog annotations. We used the ortholog annotations implemented in RefSeq instead of those from the TOGA pipeline: both employ synteny conservation. We have coordinated the identified orthologs with our gene loss criteria–absence from all the species used in a particular taxon–and excluded 268 genes from the original elusive gene set. These genes contain those missing in the previous gene annotations used in the original manuscript but present in the latest ones, as well as those falsely missing due to incorrect inference of gene trees. Finally, the refined set of 813 elusive genes were subject to comparisons with the non-elusive genes. Importantly, these comparisons retained the significantly different trends of the particular genomic, transcriptomic, and epigenomic features between them except for very few cases (Table R1 included below). This indicates that both initial and revised sets of the elusive genes reflect the nature of the ‘elusiveness,’ though the initial set contained some noises. We have modified the numbers of elusive genes in the corresponding parts of the manuscript including figures and tables. Additionally, we have added the validation procedures in Methods.

Table R1. Difference in statistical significances across different elusive gene sets *The other features showed significantly different trends between the elusive and non-elusive genes for all of the elusive gene sets and thus are not included in this table.

(P38 in Methods) The gene loss events inferred by molecular phylogeny were further assessed by synteny-based ortholog annotations implemented in RefSeq, as well as a homolog search in the genome assemblies (Table S2) with TBLASTN v2.11.0+ (Altschul et al., 1997) and MMSeqs2 (Steinegger and Söding, 2017) referring to the latest RefSeq gene annotations (last accessed on 2 Dec, 2022). This procedure resulted in the identification of 813 elusive genes that harbored three or fewer duplicates. Similarly, we extracted 8,050 human genes whose orthologs were found in all the mammalian species examined and defined them as non-elusive genes.

The reviewer also suggested us investigating falsely-missing genes due to frameshift mutations (in this case we guess that the reviewer assumed the genome assembly that falsely included frameshift mutations). This requires us to search for the orthologs by revisiting the sequencing reads because the frameshift is sometimes caused by indels of erroneous basecalling. We have selected five elusive genes and searched for the fragments of orthologs in sequencing reads for the species in which they are missing. We have retrieved sequencing reads corresponding to the genome assemblies from NCBI SRA and performed sequence similarity search using the program Diamond against the amino acid sequences of the elusive genes and could not find the frameshift that potentially causes the mis-annotation of the elusive genes.

Along this line, we noticed that when annotation files were pooled together via CD-Hit clustering, a 100% identity threshold was chosen (Methods). Since some of the pooled annotations were drawn from less high quality assemblies which yield higher likelihoods of mismatches between annotations, enforcing a 100% identity threshold will artificially remove genes due to this strict constraint. It will be paramount for this study to test the robustness of their findings when 90% and 95% identity thresholds were selected.

cd-hit clustering with 100% sequence identity only clusters those with identical (and sometimes truncated) sequences, and, in the cluster, the sequences other than the representative are discarded. This means that the sequences remain if they are not identical to the other ones. If the similarity threshold is lowered, both identical and highly similar sequences are clustered with each other, and more sequences are discarded. Therefore, our approach that employs clustering with 100% similarity may minimize false positive gene loss.

While some statistical tests were applied (although we do recommend consulting a professional statistician, since some identical distributions tend to show significantly low p-values), the authors fail to discuss the fact that their elusive gene set comprises of ~5% of all human genes (assuming 21,000 genes), while their non-elusive set represents ~40% of all genes. In other words, the authors compare their sequence and genomic features against the genomic background rather than a biological signal (nonelusiveness). An analysis whereby 1,081 genes (same number as elusive set) are randomly sampled from the 21,000 gene pool is compared against the elusive and non-elusive distributions for all presented results will reveal whether the non-elusive set follows a background distribution (noise) or not.

Our study aims to elucidate the characteristics of genes that differentiate their fates, retention or loss. To achieve this, we put this characterization into the comparison between the elusive and non-elusive genes. This comparison highlighted clearly different phylogenetic signals for gene loss between elusive and non-elusive genes, allowing us to extract the features associated with the loss-prone nature. The random sampling set suggested by Reviewer may largely consists of the remainders that were not classified by the elusive and non-elusive genes. However, these remainders may contain a considerable number of genes with distinctive phylogenetic signatures rather than the intermediates between the elusive and nonelusive genes: the genes with multiple loss events in more restricted taxa than our criterion, the ones with frequent duplication, etc. Therefore, we think that a comparison of the elusive genes with the random-sampling set does not achieve our objective: the comparison of the clearly different phylogenetic signals.

We also wondered whether the authors considered testing the links between recombination rate / LD and the genomic locations of their elusive genes (again compared against randomly sampled genes)?

We have retrieved fine-scale recombination rate data of males and females from https://www.decode.com/addendum/ (Suppl. Data of Kong, A et al., Nature, 467:1099–1103, 2010) and have compared them between the gene regions of the elusive and non-elusive genes. Both comparisons show no significant differences: average 0.829 and 0.900 recombinations/kb for the elusive and non-elusive genes, respectively, p=0.898, for males; average 0.836 and 0.846 recombinations/kb for the elusive and non-elusive genes, respectively, p=0.256, for females).

Given the evidence presented in Figure 6b, we do not agree with the statement (l.334-336): "These observations suggest that the elusive genes are unlikely to be regulated by distant regulatory elements". Here, a data population of ~1k genes is compared against a data population of ~8k genes and the presented difference between distributions could be a sample size artefact. We strongly recommend retesting this result with the ~1k randomly sampled genes from the total ~21,000 gene pool and then compare the distributions.

Analogous random sampling analysis should be performed for Fig 6a,d

As described above, our study does not intend to extract signals from background. To make the comparison objectives clear, we have revised the corresponding sentence as below.

(P22, Transcriptomic natures of elusive genes in Results) These observations suggest that the elusive genes are unlikely to be regulated by distant regulatory elements compared with the non-elusive genes (Figure 6b).

We didn't see a clear pattern in Figure 7. Please quantify enrichments with statistical tests. Even if there are enriched regions, why did the authors choose a Shannon entropy cutoff configuration of <1 (low) and >1 (high)? What was the overall entropy value range? If the maximum entropy value was 10 or 100 or even more, then denoting <1 as low and >1 as high seems rather biased.

To use Figure 7 in a new section in Results, we have added an ideogram showing the distribution of the genes that retain the chicken orthologs in microchromosomes. In response to the comment by Reviewer 2, we have performed statistical tests and found that the elusive genes were significantly more abundant in orthologs in microchromosomes than the non-elusive genes. Furthermore, the observation that the elusive genes prefer to be located in gene-rich regions was already statistically supported (Figure 2f).

As shown in Figure 5, Shannon’s H' ranged from zero to approximately 4 (exact maximum value is 3.97) and 5 (5.11) for the GTEx and Descartes gene expression datasets, respectively. Although the threshold H'=1 was an arbitrarily set, we think that it is reasonable to classify the genes with high pleiotropy from those with low pleiotropy.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Wei & Robles et al seek to estimate the heritability contribution of Neanderthal Informative Markers (NIM) relative to SNPs that arose in modern humans (MH). This is a question that has received a fair amount of attention in recent studies, but persistent statistical limitations have made some prior results difficult to interpret. Of particular concern is the possibility that heritability (h^2) attributed to Neanderthal markers might be tagging linked variants that arose in modern humans, resulting in overestimation of h^2 due to Neanderthal variants. Neanderthal variants also tend to be rare, and estimating the contribution of rare alleles to h^2 is challenging. In some previous studies, rare alleles have been excluded from h^2 estimates.

Wei & Robles et al develop and assess a method that estimates both total heritability and per-SNP heritability of NIMs, allowing them to test whether NIM contributions to variation in human traits are similar or substantially different than modern human SNPs. They find an overall depletion of heritability across the traits that they studied, and found no traits with enrichment of heritability due to NIMs. They also developed a 'fine-mapping' procedure that aims to find potential causal alleles and report several potentially interesting associations with putatively functional variants.

Strengths of this study include rigorous assessment of the statistical methods employed with simulations and careful design of the statistical approaches to overcome previous limitations due to LD and frequency differences between MH and NIM variants. I found the manuscript interesting and I think it makes a solid contribution to the literature that addresses limitations of some earlier studies.

My main questions for the authors concern potential limitations of their simulation approach. In particular, they describe varying genetic architectures corresponding to the enrichment of effects among rare alleles or common alleles. I agree with the authors that it is important to assess the impact of (unknown) architecture on the inference, but the models employed here are ad hoc and unlikely to correspond to any mechanistic evolutionary model. It is unclear to me whether the contributions of rare and common alleles (and how these correspond with levels of LD) in real data will be close enough to these simulated schemes to ensure good performance of the inference.

In particular, the common allele model employed makes 90% of effect variants have frequencies above 5% -- I am not aware of any evolutionary model that would result in this outcome, which would suggest that more recent mutations are depleted for effects on traits (of course, it is true that common alleles explain much more h^2 under neutral models than rare alleles, but this is driven largely by the effect of frequency on h^2, not the proportion of alleles that are effect alleles). Likewise, the rare allele model has the opposite pattern, with 90% of effect alleles having frequencies under 5%. Since most alleles have frequencies under 5% anyway (~58% of MH SNPs and ~73% of NIM SNPs) this only modestly boosts the prevalence of low frequency effect alleles relative to their proportion. Some selection models suggest that rare alleles should have much bigger effects and a substantially higher likelihood of being effect alleles than common alleles. I'm not sure this situation is well-captured by the simulations performed. With LD and MAF annotations being applied in relatively wide quintile bins, do the authors think their inference procedure will do a good job of capturing such rare allele effects? This seems particularly important to me in the context of this paper, since the claim is that Neanderthal alleles are depleted for overall h^2, but Neanderthal alleles are also disproportionately rare, meaning they could suffer a bigger penalty. This concern could be easily addressed by including some simulations with additional architectures to those considered in the manuscript.

We thank the reviewers for their thoughtful comments regarding rare alleles, and we agree that our RARE simulations only moderately boosted the enrichment of rare alleles in causal mutations. To address this, we added new simulations, ULTRA RARE, in which SNPs with MAF < 0.01 constitute 90% of the causal variants. Similar to our previous simulations, we use 100,000 and 10,000 causal variants to mimic highly polygenic and moderately polygenic phenotypes, and 0.5 and 0.2 for high and moderately heritable phenotypes. We similarly did three replicated simulations for each combination and partitioned the heritability with Ancestry only annotation, Ancestry+MAF annotation, Ancestry+LD annotation, and Ancestry+MAF+LD annotation. Our Ancestry+MAF+LD annotation remains calibrated in this setting (see Figure below). We believe this experiment strengthens our paper and have added it as Fig S2.

While we agree that these architectures are ad-hoc and are unlikely to correspond to realistic evolutionary scenarios, we have chosen these architectures to span the range of possible architecture so that the skew towards common or rare alleles that we have explored are extreme. The finding that our estimates are calibrated across the range that we have explored leads us to conclude that our inferences should be robust.

More broadly, we concur with the reviewer that our results (as well as others in the field) may need to be revisited as our view of the genetic architecture of complex traits evolves. The methods that we propose in this paper are general enough to explore such architectures in the future by choosing a sufficiently large set of annotations that match the characteristics across NIMs and MH SNPs. A practical limitation to this strategy is that the use of a large number of annotations can result in some annotations being assigned a small number of SNPs which would, in turn, reduce the precision of our estimates. This limitation is particularly relevant due to the smaller number of NIMs compared to MH SNPs (around 250K vs around 8M).

Reviewer #2 (Public Review):

The goal of the work described in this paper is to comprehensively describe the contribution of Neanderthal-informative mutations (NIMs) to complex traits in modern human populations. There are some known challenges in studying these variants, namely that they are often uncommon, and have unusually long haplotype structures. To overcome these, the authors customized a genotyping array to specifically assay putative Neanderthal haplotypes, and used a recent method of estimating heritability that can explicitly account for differences in MAF and LD.

This study is well thought-out, and the ability to specifically target the genotyping array to the variants in question and then use that information to properly control for population structure is a massive benefit. The methodology also allowed them to include rarer alleles that were generally excluded from previous studies. The simulations are thorough and convincingly show the importance of accounting for both MAF and LD in addition to ancestry. The fine-mapping done to disentangle effects between actual Neanderthal variants and Modern human ones on the same haplotype also seems reasonable. They also strike a good balance between highlighting potentially interesting examples of Neanderthal variants having an effect on phenotype without overinterpreting association-based findings.

The main weakness of the paper is in its description of the work, not the work itself. The paper currently places a lot of emphasis on comparing these results to prior studies, particularly on its disagreement with McArthur, et al. (2021), a study on introgressed variant heritability that was also done primarily in UK Biobank. While they do show that the method used in that study (LDSR) does not account for MAF and LD as effectively as this analysis, this work does not support the conclusion that this is a major problem with previous heritability studies. McArthur et al. in fact largely replicate these results that Neanderthal variants (and more generally regions with Neanderthal variants) are depleted of heritability, and agree with the interpretation that this is likely due to selection against Neanderthal alleles. I actually find this a reassuring point, given the differences between the variant sets and methods used by the two studies, but it isn't mentioned in the text. Where the two studies differ is in specifics, mainly which loci have some association with human phenotypes; McArthur et al. also identified a couple groups of traits that were exceptions to the general rule of depleted heritability. While this work shows that not accounting for MAF and LD can lead to underestimating NIM heritability, I don't follow the logic behind the claim that this could lead to a false positive in heritability enrichment (a false negative would be more likely, surely?). There are also more differences between this and previous heritability studies than just the method used to estimate heritability, and the comparisons done here do not sufficiently account for these. A more detailed discussion to reconcile how, despite its weaknesses, LDSR picks up similar broad patterns while disagreeing in specifics is merited.

We agree with the reviewer that our results are generally concordant with those of McArthur et al. 2021 and this concordance is reassuring given the differences across our studies. The differences across the studies, wherein McArthur et al. 2021 identify a few traits with elevated heritability while we do not, could arise due to reasons beyond the methodological differences such as differences in the sets of variants analyzed. We have partially explored this possibility in the revised manuscript by analyzing the set of introgressed variants identified by the Sprime method (which was used in McArthur et al. 2021) using our method: we continue to observe a pattern of depletion with no evidence for enrichment. We hypothesize that the reason why LDSR picks up similar overall patterns despite its limitations is indicative of the nature of selection on introgressed alleles (which, in turn, influences the dependence of effect size on allele frequency and LD). Investigating this hypothesis will require a detailed understanding of the LDSR results on parameters such as the MAF threshold on the regression SNPs and the LD reference SNPs and the choice of the LD reference panel.

Not accounting for MAF and LD can underestimate NIM heritability but can both underestimate and overestimate heritability at MH SNPs. Hence, tests that compare per-SNP heritability at NIMs to MH SNPs can therefore lead to false positives both in the direction of enrichment and depletion.

We have now written in the Discussion: “In spite of these differences in methods and NIMs analyzed, our observation of an overall pattern of depletion in the heritability of introgressed alleles is consistent with the findings of McArthur et al. The robustness of this pattern might provide insights into the nature of selection against introgressed alleles”

In general this work agrees with the growing consensus in the field that introgressed Neanderthal variants were selected against, such that those that still remain in human populations do not generally have large effects on phenotypes. There are exceptions to this, but for the most part observed phenotypic associations depend on the exact set of variants being considered, and, like those highlighted in this study, still lack more concrete validation. While this paper does not make a significant advance in this general understanding of introgressed regions in modern populations, it does increase our knowledge in how best to study them, and makes a good attempt at addressing issues that are often just mentioned as caveats in other studies. It includes a nice quantification of how important these variables are in interpreting heritability estimates, and will be useful for heritability studies going forward.

Author Response:

Reviewer #1 (Public Review):

In this manuscript, the authors leverage novel computational tools to detect, classify and extract information underlying sharp-wave ripples, and synchronous events related to memory. They validate the applicability of their method to several datasets and compare it with a filtering method. In summary, they found that their convolutional neural network detection captures more events than the commonly used filter method. This particular capability of capturing additional events which traditional methods don't detect is very powerful and could open important new avenues worth further investigation. The manuscript in general will be very useful for the community as it will increase the attention towards new tools that can be used to solve ongoing questions in hippocampal physiology.

We thank the reviewer for the constructive comments and appreciation of the work.

Additional minor points that could improve the interpretation of this work are listed below:

• Spectral methods could also be used to capture the variability of events if used properly or run several times through a dataset. I think adjusting the statements where the authors compare CNN with traditional filter detections could be useful as it can be misleading to state otherwise.

We thank the reviewer for this suggestion. We would like to emphasize that we do not advocate at all for disusing filters. We feel that a combination of methods is required to improve our understanding of the complex electrophysiological processes underlying SWR. We have adjusted the text as suggested. In particular, a) we removed the misleading sentence from the abstract, and instead declared the need for new automatic detection strategies; b) we edited the introduction similarly, and clarified the need for improved online applications.

• The authors show that their novel method is able to detect "physiological relevant processes" but no further analysis is provided to show that this is indeed the case. I suggest adjusting the statement to "the method is able to detect new processes (or events)".

We have corrected text as suggested. In particular, we declare that “The new method, in combination with community tagging efforts and optimized filter, could potentially facilitate discovery and interpretation of the complex neurophysiological processes underlying SWR.” (page 12).

• In Fig.1 the authors show how they tune the parameters that work best for their CNN method and from there they compare it with a filter method. In order to offer a more fair comparison analogous tuning of the filter parameters should be tested alongside to show that filters can also be tuned to improve the detection of "ground truth" data.

Thank you for this comment. As explained before, see below the results of the parameter study for the filter in the very same sessions used for training the CNN. The parameters chosen (100- 300Hz band, order 2) provided maximal performance in the test set. Therefore, both methods are similarly optimized along training. This is now included (page 4): “In order to compare CNN performance against spectral methods, we implemented a Butterworth filter, which parameters were optimized using the same training set (Fig.1-figure supplement 1D).”

• Showing a manual score of the performance of their CNN method detection with false positive and false negative flags (and plots) would be clarifying in order to get an idea of the type of events that the method is able to detect and fails to detect.

We have added information of the categories of False Positives for both the CNN and the filter in the new Fig.4F. We have also prepared an executable figure to show examples and to facilitate understanding how the CNN works. See new Fig.5 and executable notebook https://colab.research.google.com/github/PridaLab/cnn-ripple-executable-figure/blob/main/cnn-ripple-false-positive-examples.ipynb

• In fig 2E the authors show the differences between CNN with different precision and the filter method, while the performance is better the trends are extremely similar and the numbers are very close for all comparisons (except for the recall where the filter clearly performs worse than CNN).

This refers to the external dataset (Grosmark and Buzsaki 2016), which is now in the new Fig.3E. To address this point and to improve statistical report, we have added more data resulting in 5 sessions from 2 rats. Data confirm better performance of CNN model versus the filter. The purpose of this figure is to show the effect of the definition of the ground truth on the performance by different methods, and also the proper performance of the CNN on external datasets without retraining. Please, note that in Grosmark and Buzsaki, SWR detection was conditioned on the

coincidence of both population synchrony and LFP definition thus providing a “partial ground truth” (i.e. SWR without population firing were not annotated in the dataset).

• The authors acknowledge that various forms of SWRs not consistent with their common definition could be captured by their method. But theoretically, it could also be the case that, due to the spectral continuum of the LFP signals, noisy features of the LFP could also be passed as "relevant events"? Discussing this point in the manuscript could help with the context of where the method might be applied in the future.

As suggested, we have mentioned this point in the revised version. In particular: “While we cannot discard noisy detection from a continuum of LFP activity, our categorization suggest they may reflect processes underlying buildup of population events (de la Prida et al., 2006). In addition, the ability of CA3 inputs to bring about gamma oscillations and multi-unit firing associated with sharp-waves is already recognized (Sullivan et al., 2011), and variability of the ripple power can be related with different cortical subnetworks (Abadchi et al., 2020; Ramirez- Villegas et al., 2015). Since the power spectral level operationally defines the detection of SWR, part of this microcircuit intrinsic variability may be escaping analysis when using spectral filters” (page 16).

• In fig. 5 the authors claim that there are striking differences in firing rate and timings of pyramidal cells when comparing events detected in different layers (compare to SP layer). This is not very clear from the figure as the plots 5G and 5H show that the main differences are when compare with SO and SLM.

We apologize for generating confusion. We meant that the analysis was performed by comparing properties of SWR detected at SO, SR and SLM using z- values scored by SWR detected at SP only). We clarified this point in the revised version: “We found larger sinks and sources for SWR that can be detected at SLM and SR versus those detected at SO (Fig.7G; z-scored by mean values of SWR detected at SP only).” (page 14).

• Could the above differences be related to the fact that the performance of the CNN could have different percentages of false-positive when applied to different layers?

The rate of FP is similar/different across layers: 0.52 ± 0.21 for SO, 0.50 ± 0.21 for SR and 0.46 ± 0.19 for SLM. This is now mentioned in the text: “No difference in the rate of False Positives between SO (0.52 ± 0.21), SR (0.50 ± 0.21) and SLM (0.46 ± 0.19) can account for this effect.” (page 12)

Alternatively, could the variability be related to the occurrence (and detection) of similar events in neighboring spectral bands (i.e., gamma events)? Discussion of this point in the manuscript would be helpful for the readers.

We have discussed this point: “While we cannot discard noisy detection from a continuum of LFP activity, our categorization suggest they may reflect processes underlying buildup of population events (de la Prida et al., 2006). In addition, the ability of CA3 inputs to bring about gamma oscillations and multi-unit firing associated with sharp-waves is already recognized (Sullivan et al., 2011), and variability of the ripple power can be related with different cortical subnetworks (Abadchi et al., 2020; Ramirez-Villegas et al., 2015).” (Page 16)

Overall, I think the method is interesting and could be very useful to detect more nuance within hippocampal LFPs and offer new insights into the underlying mechanisms of hippocampal firing and how they organize in various forms of network events related to memory.

We thank the reviewer for constructive comments and appreciation of the value of our work.

Reviewer #2 (Public Review):

Navas-Olive et al. provide a new computational approach that implements convolutional neural networks (CNNs) for detecting and characterizing hippocampal sharp-wave ripples (SWRs). SWRs have been identified as important neural signatures of memory consolidation and retrieval, and there is therefore interest in developing new computational approaches to identify and characterize them. The authors demonstrate that their network model is able to learn to identify SWRs by showing that, following the network training phase, performance on test data is good. Performance of the network varied by the human expert whose tagging was used to train it, but when experts' tags were combined, performance of the network improved, showing it benefits from multiple input. When the network trained on one dataset is applied to data from different experimental conditions, performance was substantially lower, though the authors suggest that this reflected erroneous annotation of the data, and once corrected performance improved. The authors go on to analyze the LFP patterns that nodes in the network develop preferences for and compare the network's performance on SWRs and non-SWRs, both providing insight and validation about the network's function. Finally, the authors apply the model to dense Neuropixels data and confirmed that SWR detection was best in the CA1 cell layer but could also be detected at more distant locations.

The key strengths of the manuscript lay in a convincing demonstration that a computational model that does not explicitly look for oscillations in specific frequency bands can nevertheless learn to detect them from tagged examples. This provides insight into the capabilities and applications of convolutional neural networks. The manuscript is generally clearly written and the analyses appear to have been carefully done.

We thank the reviewer for the summary and for highlighting the strengths of our work.

While the work is informative about the capabilities of CNNs, the potential of its application for neuroscience research is considerably less convincing. As the authors state in the introduction, there are two potential key benefits that their model could provide (for neuroscience research): 1. improved detection of SWRs and 2. providing additional insight into the nature of SWRs, relative to existing approaches. To this end, the authors compare the performance of the CNN to that of a Butterworth filter. However, there are a number of major issues that limit the support for the authors' claims:

Please, see below the answers to specific questions, which we hope clarify the validity of our approach

• Putting aside the question of whether the comparison between the CNN and the filter is fair (see below), it is unclear if even as is, the performance of the CNN is better than a simple filter. The authors argue for this based on the data in Fig. 1F-I. However, the main result appears to be that the CNN is less sensitive to changes in the threshold, not that it does better at reasonable thresholds.

This comment now refers to the new Fig.2A (offline detection) and Fig.2C,D (online detection). Starting from offline detection, yes, the CNN is less sensitive than the filter and that has major consequences both offline and online. For the filter to reach it best performance, the threshold has to be tuned which is a time-consuming process. Importantly, this is only doable when you know the ground truth. In practical terms, most lab run a semi-automatic detection approach where they first detect events and then they are manually validated. The fact that the filter is more sensible to thresholds makes this process very tedious. Instead, the CNN is more stable.

In trying to be fair, we also tested the performance of the CNN and the filter at their best performance (i.e. looking for the threshold f¡providing the best matching with the ground truth). This is shown at Fig.3A. There are no differences between methods indicating the CNN meet the gold standard provided the filter is optimized. Note again this is only possible if you know the ground truth because optimization is based in looking for the best threshold per session.

Importantly, both methods reach their best performance at the expert’s limit (gray band in Fig.3A,B). They cannot be better than the individual ground truth. This is why we advocate for community tagging collaborations to consolidate sharp-wave ripple definitions.

Moreover, the mean performance of the filter across thresholds appears dramatically dampened by its performance on particularly poor thresholds (Fig. F, I, weak traces). How realistic these poorly tested thresholds are is unclear. The single direct statistical test of difference in performance is presented in Fig. 1H but it is unclear if there is a real difference there as graphically it appears that animals and sessions from those animals were treated as independent samples (and comparing only animal averages or only sessions clearly do not show a significant difference).

Please, note this refers to online detection. We are not sure to understand the comment on whether the thresholds are realistic. To clarify, we detect SWR online using thresholds we similarly optimize for the filter and the CNN over the course of the experiment. This is reported in Fig.2C as both, per session and per animals, reaching statistical differences (we added more experiments to increase statistical power). Since, online defined thresholds may still not been the best, we then annotated these data and run an additional posthoc offline optimization analysis which is presented in Fig.2D. We hope this is now more clear in the revised version.

Finally, the authors show in Fig. 2A that for the best threshold the CNN does not do better than the filter. Together, these results suggest that the CNN does not generally outperform the filter in detecting SWRs, but only that it is less sensitive to usage of extreme thresholds.

We hope this is now clarified. See our response to your first bullet point

Indeed, I am not convinced that a non-spectral method could even theoretically do better than a spectral method to detect events that are defined by their spectrum, assuming all other aspects are optimized (such as combining data from different channels and threshold setting)

As can be seen in the responses to the editor synthesis, we have optimized the filter parameter similarly (new Fig.1-supp-1D) and there is no improvement by using more channels (see below). In any case, we would like to emphasize that we do not advocate at all for disusing filters. We feel that a combination of methods is required to improve our understanding of the complex electrophysiological processes underlying SWR.

• The CNN network is trained on data from 8 channels but it appears that the compared filter is run on a single channel only. This is explicitly stated for the online SWR detection and presumably, that is the case for the offline as well. This unfair comparison raises the possibility that whatever improved performance the CNN may have may be due to considerably richer input and not due to the CNN model itself. The authors state that a filter on the data from a single channel is the standard, but many studies use various "consensus" heuristics, e.g. in which elevated ripple power is required to be detected on multiple channels simultaneously, which considerably improves detection reliability. Even if this weren't the case, because the CNN learns how to weight each channel, to argue that better performance is due to the nature of the CNN it must be compared to an algorithm that similarly learns to optimize these weights on filtered data across the same number of channels. It is very likely that if this were done, the filter approach would outperform the CNN as its performance with a single channel is comparable.

We appreciate this comment. Using one channel to detect SWR is very common for offline detection followed by manual curation. In some cases, a second channel is used either to veto spurious detections (using a non-ripple channel) or to confirm detection (using a second ripple channel and/or a sharp-wave) (Fernandez-Ruiz et al., 2019). Many others use detection of population firing together with the filter to identify replay (such as in Grosmark and Buzsaki 2019, where ripples were conditioned on the coincidence of both population firing and LFP detected ripples). To address this comment, we compared performance using different combinations of channels, from the standard detection at the SP layer (pyr) up to 4 and 8 channels around SP using the consensus heuristics. As can be seen filter performance is consistent across configurations and using 8 channels is not improving detection. We clarify this in the revised version: ”We found no effect of the number of channels used for the filter (1, 4 and 8 channels), and chose that with the higher ripple power” (see caption of Fig.1-supp-1D).

• Related to the point above, for the proposed CNN model to be a useful tool in the neuroscience field it needs to be amenable to the kind of data and computational resources that are common in the field. As the network requires 8 channels situated in close proximity, the network would not be relevant for numerous studies that use fewer or spaced channels. Further, the filter approach does not require training and it is unclear how generalizable the current CNN model is without additional network training (see below). Together, these points raise the concern that even if the CNN performance is better than a filter approach, it would not be usable by a wide audience.

Thank you for this comment. To handle with different input channel configurations, we have developed an interpolation approach, which transform any data into 8-channel inputs. We are currently applying the CNN without re-training to data from several labs using different electrode number and configurations, including tetrodes, linear silicon probes and wires. Results confirm performance of the CNN. Since we cannot disclose these third-party data here, we have looked for a new dataset from our own lab to illustrate the case. See below results from 16ch silicon probes (100 um inter-electrode separation), where the CNN performed better than the filter (F1: p=0.0169; Precision, p=0.0110; 7 sessions, from 3 mice). We found that the performance of the CNN depends on the laminar LFP profile, as Neuropixels data illustrate.

• A key point is whether the CNN generalizes well across new datasets as the authors suggest. When the model trained on mouse data was applied to rat data from Grosmark and Buzsaki, 2016, precision was low. The authors state that "Hence, we evaluated all False Positive predictions and found that many of them were actually unannotated SWR (839 events), meaning that precision was actually higher". How were these events judged as SWRs? Was the test data reannotated?

We apologize for not explaining this better in the original version. We choose Grosmark and Buzsaki 2016 because it provides an “incomplete ground truth”, since (citing their Methods) “Ripple events were conditioned on the coincidence of both population synchrony events, and LFP detected ripples”. This means there are LFP ripples not included in their GT. This dataset provides a very good example of how the experimental goal (examining replay and thus relying in population firing plus LFP definitions) may limit the ground truth.

Please, note we use the external dataset for validation purposes only. The CNN model was applied without retraining, so it also helps to exemplify generalization. Consistent with a partial ground truth, the CNN and the filter recalled most of the annotated events, but precision was low. By manually validating False Positive detections, we re-annotated the external dataset and both the CNN and the filter increased precision.

To make the case clearer, we now include more sessions to increase the data size and test for statistical effects (Fig.3E). We also changed the example to show more cases of re-annotated events (Fig.3D). We have clarified the text: “In that work, SWR detection was conditioned on the coincidence of both population synchrony and LFP definition, thus providing a “partial ground truth” (i.e. SWR without population firing were not annotated in the dataset).” (see page 7).

• The argument that the network improves with data from multiple experts while the filter does not requires further support. While Fig. 1B shows that the CNN improves performance when the experts' data is combined and the filter doesn't, the final performance on the consolidated data does not appear better in the CNN. This suggests that performance of the CNN when trained on data from single experts was lower to start with.

This comment refers to the new Fig.3B. We apologize for not have had included a between- method comparison in the original version. To address this, we now include a one-way ANOVA analysis for the effect of the type of the ground truth on each method, and an independent one- way ANOVA for the effect of the method in the consolidated ground truth. To increase statistical power we have added more data. We also detected some mistake with duplicated data in the original figure, which was corrected. Importantly, the rationale behind experts’ consolidated data is that there is about 70% consistency between experts and so many SWR remain not annotated in the individual ground truths. These are typically some ambiguous events, which may generate discussion between experts, such as sharp-wave with population firing and few ripple cycles. Since the CNN is better in detecting them, this is the reason supporting they improve performance when data from multiple experts are integrated.

Further, regardless of the point in the bullet point above, the data in Fig. 1E does not convincingly show that the CNN improves while the filter doesn't as there are only 3 data points per comparison and no effect on F1.

Fig.1E shows an example, so we guess the reviewer refers to the new Fig.2C, which show data on online operation, where we originally reported the analysis per session and per animal separately with only 3 mice. We have run more experiments to increase the data size and test for statistical effects (8 sessions, 5 mice; per sessions p=0.0047; per mice p=0.033; t-test). This is now corrected in the text and Fig.1C, caption. Please, note that a posthoc offline evaluation of these online sessions confirmed better performance of the CNN versus the filter, for all normalized thresholds (Fig.2D).

• Apart from the points above regarding the ability of the network to detect SWRs, the insight into the nature of SWRs that the authors suggest can be achieved with CNNs is limited. For example, the data in Fig. 3 is a nice analysis of what the components of the CNN learn to identify, but the claim that "some predictions not consistent with the current definition of SWR may identify different forms of population firing and oscillatory activities associated to sharp-waves" is not thoroughly supported. The data in Fig. 4 is convincing in showing that the network better identifies SWRs than non-SWRs, but again the insight is about the network rather than about SWRs.

In the revised version, have now include validation of all false positives detected by the CNN and the filter (Fig.4F). To facilitate the reader examining examples of True Positive and False Positive detection we also include a new figure (Fig.5), which comes with the executable code (see page 9). We also include comparisons of the features of TP events detected by both methods (Fig.2B), where is shown that SWR events detected by the CNN exhibited features more similar to those of the ground truth (GT), than those detected by the filter. We feel the entire manuscript provides support to these claims.

Finally, the application of the model on Neuropixels data also nicely demonstrates the applicability of the model on this kind of data but does not provide new insight regarding SWRs.

We respectfully disagree. Please, note that application to ultra-dense Neuropixels not only apply the model to an entirely new dataset without retraining, but it shows that some SWR with larger sinks and sources can be actually detected at input layers (SO, SR and SLM). Importantly, those events result in different firing dynamics providing mechanistic support for heterogeneous behavior underlying, for instance, replay.

In summary, the authors have constructed an elegant new computational tool and convincingly shown its validity in detecting SWRs and applicability to different kinds of data. Unfortunately, I am not convinced that the model convincingly achieves either of its stated goals: exceeding the performance of SWR detection or providing new insights about SWRs as compared to considerably simpler and more accessible current methods.

We thank you again for your constructive comments. We hope you are now convinced on the value of the new method in light to the new added data.

Author Response

Reviewer #1 (Public Review):

This paper by Zhuang and colleagues seeks to answer an important clinical question by trying to come up with novel predictive biomarkers to predict high-risk T1 colorectal cancers that are at risk for nodal involvement. The current clinical features may both miss patients who underwent local therapy and who should have gone on to have surgery and patients for whom surgery was done based on risk features but perhaps unnecessarily. Using a training and validation set, they developed a protein-based classifier with an AUC of 0.825 based on mass spec analyses and proteomic analyses of patients with and without LN importantly linking biological rationale to the proteomic discoveries.

In the training cohort, they took 105 candidate proteins reduced to 55, and did a validation in the training cohort first and then in two validation cohorts (one of which was prospective). They also looked at a 9-protein classifier which also performed well and furthermore looked at IHC for clinical ease.

We appreciate the reviewers for the positive review and valuable comments. We have revised the manuscript according to the comments.

Reviewer #2 (Public Review):

The authors utilized a label-free LC-MS/MS analysis in formalin-fixed paraffin-embedded (FFPE) tumors from 143 LNM-negative and 78 LNM-positive patients with T1 CRC to identify protein biomarkers to determine LNM in T1 CRC.

The authors used a fair number of clinical samples for the proteomics investigation. The experimental design is reasonable, and the statistical methods used in this manuscript are solid.

The authors largely achieved their aims and the results supported their conclusion. The method used in this proteomic study can also be used for the proteomics analysis of other cancer types to identify diagnostic and prognostic biomarkers. In addition, the 9-marker panel has a potential clinical diagnosis practice in determining LNM in T1 CRC.

Nevertheless, the authors need to justify their standards in selecting the biomarkers. For example, a p-value cut-off of 0.1 is not a usual criterion in similar proteomic studies. In addition, an identification frequency of 30% in patients seems not preferable for biomarker identification. The authors also need to justify the definition of fold change in the three subtypes with Kruskal-Walli's test. The authors need to describe more details on how they identified the 13 proteins from a 55-protein database. In addition, what is the connection between the final 9 proteins and the 19 proteins? What is the criterion to select 5 proteins for IHC validation from the 9 proteins?

We appreciate the reviewers for the positive review and valuable comments. We have revised the manuscript according to the comments.

The criteria and details of our standards in selecting are as follows.

1) About p-value cut-off of 0.1:

The purpose of this step is to screen appropriate variables for subsequent machine learning, rather than comparing differences between groups. The p-value cut-off of 0.1 is also a reliable strategy for variable selection in proteomics research. For example, it has been used in studies to predict the response to tumor necrosis factor-α inhibitors in rheumatoid arthritis (PMID: 28650254); the research about circadian clock in mouse liver (PMID: 29674717); the proteomic biomarker discovery in atherosclerosis (PMID: 15496433); and the proteomics and transcriptomics analysis in bacillus subtilis (PMID: 19948795).

Based on reviewer’s suggestion, we used a cutoff of p-value 0.05 to screen for variables. In a training set of 70 lymph node-negative and 62 lymph node-positive cases, we identified 355 protein markers. We further incorporated these proteins into a lasso regression analysis and ultimately developed a lymph node metastasis prediction model consisting of 52 protein markers. We validated the model in VC1 and VC2, with AUC values of 1.000, 0.824, and 0.918 for the training set, VC1, and VC2, respectively, the predictive performance was slightly inferior to that of the model developed in this study (Figure 3- figure supplement 1C).

2) About identification frequency of 30%:

The analysis focusing on the proteins identified in > 30% of the samples has been applied in the previous published studies. For instance, the study of using proteomic biomarkers to build diagnostic model in lung cancer (PMID: 29576497), proteins identified in > 30% cohort samples were used for downstream analysis. In the study on the impact of Reptin on protein-protein interaction (PMID: 30862565) have demonstrated that proteins were required to have at least in > 30% of samples in order to be included in the proteome dataset.

We compared our cohort with Jun Qin et al. and Bing Zhang et al., study published in Nature (PMID: 25043054), according to the number of the proteins detected in more than 10%, 20%, 30%, 40%, 50%, 60%, 70%, 80%, 90%, 100% of samples, respectively (Figure 2- figure supplement 1). The proportion proteins detected at different cutoff of the samples in the three cohort were, 10% (0.60, 0.94, 0.48), 20% (0.52, 0.83, 0.38), 30% (0.46,0.75, 0.31), 40% (0.41, 0.69, 0.26), 50% (0.37, 0.63, 0.23), 60% (0.33, 0.57, 0.18), 70% (0.29, 0.52, 0.15), 80% (0.25, 0.45, 0.11), 90% (0.19, 0.37, 0.11), 100% (0.07, 0.23, 0.10), respectively. The results showed that our cohort was reliable.

To investigate the impacts of protein identification frequency cutoff in our study, we performed comparative pathway enrichment analysis of the differential expressed proteins (LNM+ vs. LNM-: p-value < 0.05, Wilcoxon rank-sum tests) under different observation percentiles, which were detected in more than 10%, more than 30% and more than 50% of samples, respectively. The results revealed that proteins from three thresholds (10%, 30% and 50%) represented similar pathway enrichment, such as mTOR signaling pathway and amino acid metabolism pathways were dominant in LNM-negative patients, coagulation cascades and Lipid metabolism pathways were overrepresented in the LNM-positive patients (Figure 2- figure supplement 1)

Based on reviewer’s suggestion, we used a cutoff of 50% as identification frequency for variables. The lasso regression was carried out in training cohort (70 LNM-negative and 62 LNM-positive), with AUC of 0.999. The model was validated in VC1 and VC2, with AUC of 0.812 and 0.886, respectively. (Figure 2- figure supplement 1).

3) About identification of the 13 proteins and the criterion to select 5 proteins for IHC validation from 55-protein database:

The process of reducing the number of proteins from 55 to 13 and finally establishing a 5-molecule classifier based on the IHC score is as shown in Figure 1- figure supplement 2 in the revision. We first selected 19 proteins with [log2FC] > 1 or < -1 and p<0.05 (Wilcoxon rank-sum test) between the LNM-negative and LNM-positive in 221 patients from 55 proteins. Then we started looking for antibodies to these 19 proteins. We finally obtained 13 antibodies for further immunohistochemistry. We did immunohistochemical staining to the FFPE samples with 13 antibodies, and got the IHC score of each protein to build the single molecular prediction model by SPSS on ROC curve. For the principles of MS based proteomic and IHC stain are different, not all identified proteins can be converted into IHC. Finally, 5 IHC makers with p-value of IHC score less than 0.05 (Student’s t-test) were selected to build the IHC classifier using Logistic Regression. We also updated the description in the “Result” section in the revised manuscript (line 718-722, page 34-35 in the revision).

4) About the connection between the final 9 proteins and the 19 proteins:

To facilitate the clinical translation of the model, Multiple Logistic Regression was used to obtain 9 core proteins from 19 proteins (Figure 1- figure supplement 2 in the revision). We first performed logistic regression in 19 proteins, and eliminated 10 proteins with insignificant Estimate Std. Error z value (Pr (>|z|) > 0.05, and obtained 9 proteins with Pr(>|z|) < 0.05. After that, we carried out Binary Logistic Regression calculation again with 9 proteins to build the simplified classifier. We also updated the description in the “Materials and methods” section in the revised manuscript (line 1092, page 51 in the revision).

5) About the definition of fold change in the three subtypes with Kruskal-Walli's test:

The fold change in the three subtypes is the ratio of the mean of the expressions in each group (well to moderately differentiated adenocarcinoma, poorly differentiated adenocarcinoma and mucinous adenocarcinoma) to the mean of the other two group. Kruskal-Walli's test was performed between three subtypes.

We also updated the description in the “Result” section in the revised manuscript (line 506-517, page 25 in the revision), and “Figure 1- figure supplement 2H in the revision”.

Reviewer #3 (Public Review):

This work provides a proteomic analysis of 132 early-stage (pT1) colorectal cancers (CRC) to attempt to identify proteins (or a signature pattern thereof) that might be used to predict the patient risk of lymph node metastases (LNM) and potentially stratify patients for further treatment or surveillance. The generated dataset is extensive and the methods appear solid. The work identifies a 55-protein signature that is strongly predictive of LNM in the training cohort and two validation cohorts and then generates two simplified classifiers: a 9-protein proteomic and a 5-protein immunohistochemical classifier. These also perform very well in predicting LNM. Loss of the small GTPase RHOT2 is identified as a poor prognostic factor and validated in a migration assay. The findings could allow better prognostication in CRC and, if confirmed and better validated and contextualized, might impact patient care.

Strengths:

A large training cohort of resected early-stage (pT1M0) CRCs was analyzed by rigorous methods including careful quantitative analysis. The data generated are unbiased and potentially useful. A number of proteins are found to be different between CRCs with and without lymph node metastases, which are used to train a machine learning model that performs flawlessly in predicting LNM in the training cohort and very well in predicting LNM in two validation cohorts. The authors then develop two simplified classifiers that might be more readily extended into clinical care: a 9-protein proteomic assay and a 5-protein immunohistochemical assay; both of these also perform well in predicting LNM. Because LNM is a key prognostic factor, and colectomy (which includes removal of lymph nodes needed to assess LNM) carries significant risk and morbidity, particularly in rectal cancer, classifiers like these are potentially interesting. Finally, the authors identify the loss of expression of RHOT2 as a novel prognostic factor.

Weaknesses:

Major points:

The data are limited by a number of assumptions about metastasis, minimal contextualization of the results, and claims that are too strong given the data. Critically, the authors use the presence or absence of LNM as the study's only outcome; while LNM is a key predictor in CRC, it is uncommon in T1 CRC (generally 3-10%, 12% in this study), stochastic, inefficient, and incompletely identified by histologic evaluation. Larger resection (here, colectomy) removes both identified and occult LNM, which is probably best studied in randomized trials of lymphadenectomy in Japanese gastric cancer cohorts and should be better discussed. Critically, patient survival or disease-free survival would be more relevant outcomes. Further, absent longer-term data, many patients without identified LNM might nonetheless be high-risk and skew the cohorts. It is also not clear whether these findings would be generalizable to other early-stage colon cancers.

The data are also not correlated with the genetics of the cases, which were not discussed.

The results would benefit from the inclusion of standard-of-care MSI status. The classifiers would also be much more impactful if they were generalizable beyond T1 CRCs; this could be readily tested in public datasets.

The authors explain the data as mechanistic, but, aside from one experiment modulating RHOT2 levels, they are fundamentally correlative and should be described as such.

Although they focused on areas containing >80% tumor as judged by the reading pathologist, it is unclear whether the identified proteomic changes originate from the tumor or the microenvironment.

The authors fail to properly contextualize the results or overstate the novelty of their study. A number of examples - the study is claimed as "the first proteomic study of T1 CRC" and "the first comprehensive proteomics study to focus on LNM in patients with submucosal T1 CRCs"; neither of these appears to be true, for example, Steffen et al. (Journal of Proteome Research, 2021, reference 18) may satisfy both of these, although the numbers are smaller. Many other results are reported without context, for example, proteomic characterization of mucinous carcinomas has been performed previously, a modest correlation in mucinous carcinoma is ascribed a large mechanistic role, and PDPN is discussed but is not contextualized as a protein that has been well-studied in the context of metastasis.

The data on RHOT2 are promising but very preliminary. RHOT2 is described as ubiquitous in colorectal cancer cell lines; a brief search in Human Protein Atlas shows RHOT2 RNA and proteins are ubiquitously expressed throughout the body. While its loss appears potentially prognostic, it is unclear whether this is simply a surrogate for other features, such as loss of differentiation state, and whether this is unique to CRC; multivariate analysis would be important.

We appreciate the reviewer for the constructive and insightful comments, which help to improve the quality of this manuscript. Here, we summarized the reviewer’s comments as following: (1) Lack of longer-term data and micrometastasis; (2) test the classifier in public datasets; (3) inclusion of standard genetics and gene alterations; (4) about the tumor purity of all tumor samples and whether the results were influenced by the tumor microenvironment; (5) contextualize the results; (6) multivariate analysis of RHOT2.

1) Lack of longer-term data and micrometastasis:

Thank the reviewer for the comments. We fully acknowledge the limitations of our study, including the uncertainty associated with the detection of lymph node micrometastasis and the lack of long-term survival data, which can impact the strength of our conclusions. We agree that LNM is a key predictor in CRC and that it is uncommon in T1 CRC, with a reported incidence of 3-10%. We acknowledge that larger resections, such as colectomy, are generally recommended for patients with T1 CRC with LNM due to the potential risk of metastasis. However, our study aimed to establish a predictive model for LNM in T1 CRC, which could potentially help guide clinical decision-making on whether additional surgery is needed after endoscopic resection, according to the current NCCN guidelines.

We have taken following methods to address these limitations:

• We matched propensity-score of patients to reduce confounding biases in our training cohort, and patients were prospectively enrolled in our validation cohort, which was designed as a single-blinded prospective study to enhance the rigor and reliability of our findings.

• For the influence of micrometastases in our study. According to reviewer's suggestion, we discussed the reports related to lymph nodes micrometastases in Japanese gastric cancer cohorts (PMID: 17377930, 9070482), and at the same time, we consulted the articles about micrometastases in T1 CRC (PMID: 17661146, 16412600). There were about 5% pT1N0 gastric cancer patients have ITCs in LN, and 10% in pT1Nx CRC. The effect of MMs on prognosis in pT1N0 CRC is still unclear. The present of ITCs/MMs in LN may explain why there are nearly 13% (29 of 221) LNM-negative patients were classified into high-risk group by the prediction model in our study.

We have also added a section to the “Discussion” in the revised manuscript to discuss the potential impact of these limitations on the interpretation of our findings (line 856-873, page 41) in the revision, as follow:

“In this study, to ensure the accuracy of LN status of the enrolled patients, the dissected number of LN in all patients including both surgical resection and ESD was more than 12. However, the longer-term follow-up data, including DFS, PFS, etc., are not available, due to limitations in sample collection time and the prognosis of such patients needs to be tracked over long periods of time, and may impact the strength of our conclusions. To address this limitation, we used propensity-score matching to reduce confounding biases in our training cohort. Patients were prospectively enrolled in our validation cohort (VC2), which was designed as a single-blinded prospective study to enhance the rigor and reliability of our findings. Furthermore, the presence of isolated tumor cells (ITCs) or micrometastases (MMs) within regional LN are not considered, due to conventional histopathologic examination cannot detected them. According to previous studies, there were about 5% pT1N0 gastric cancer patients have ITCs in LN, and 10% in pT1Nx CRC. The effect of MMs on prognosis in pT1N0 CRC is still unclear. The present of ITCs/MMs in LN may explain why there are nearly 13% (29 of 221) LNM-negative patients were classified into high-risk group by the prediction model in our study. Our study would provide a valuable database and could help for clinical decision-making in the context of T1 CRC. We will continuously follow the prognosis of the patients, and the ITCs/MMs in LN also need to be further validated in the future studies.”

In conclusion, we appreciate reviewer’s comments and acknowledge the limitations of our study. We believe that our study provides valuable insights into the development of a predictive model for LNM in T1 CRC, which could potentially aid in clinical decision-making according to the current NCCN guidelines.

2) Test the classifier in public datasets:

According to reviewer’s suggestions, we tested our classifier in two different public datasets, including the colon and rectal cancer study from CPTAC published in Nature (PMID: 25043054), and the metastatic colorectal cancer study published in Cancer Cell (PMID: 32888432). The detail was further discussed in “point-to-point responses R3 Q2.”.

3) Standard genetics and gene alterations:

According to reviewer’s suggestions, we assessed MSI status and CRC-associated gene mutations (RAS, BRAF and PIK3CA) in our cohort. The detail was further discussed in “point-to-point responses R3 Q1.”

4) The influence of microenvironment:

We apologized for not explaining it clearly. To the question of whether the differences between two groups (LNM+ and LNM-) are caused by tumor microenvironment or the tumor tissues, we firstly, used xCell (PMID: 29141660) to study the composition of the tumor microenvironment (Figure2-source data 4 in the revision). The results showed that there was no difference in the tumor microenvironment between the LNM-positive and negative groups (P > 0.05, Wilcoxon rank-sum test) (Figure RL1A). However, when we compared the xCell algorism-based cell deconvolution results between the LNM-positive and -negative groups, we found 8 microenvironment associated cell features differed in two groups (p<0.05) (Figure RL1B). LNM-positive patients were featured with Chondrocytes and Th1 cells. And the remaining 6 features are all high in LNM-negative patients, including, B cells, cDC, Myocytes, etc. Correspondingly, 7 immune cell markers were also observed to be significantly different between the two groups (Log2FC>1 or <-1, P > 0.05, Wilcoxon rank-sum test) (Figure RL1C).

Secondly, we checked the expression profile of the signature proteins detected in our study by The Human Protein Atlas (HPA). Among 9404 identified proteins, 7852 (83.4%) have HPA’s CRC IHC staining data, and 6249 (79.6%) showed medium to high tumor-specific staining in CRC samples (Figure RL1D). Of the signature proteins up-regulated in LNM-positive patients (LNM+ vs. LNM-: log2FC > 1 and p<0.05, Wilcoxon rank-sum test), 76 of 84 (90.5%) have IHC staining data in HPA, and 63 (82.9%) showed medium to high tumor-specific staining in CRC samples (Figure RL1E). For specific proteins of LNM-negative patients (LNM+ vs. LNM-: log2FC <-1 and p<0.05, Wilcoxon rank-sum test), 72 of 82 (87.8%) have IHC staining data in HPA, and 60 (83.3%) showed medium to high tumor-specific staining in CRC samples (Figure RL1F).

Finally, we reviewed again all H&E-stained slides of tumor tissues of patients involved in the study, and supplemented tumor purity values of tumor samples of all the patients in Figure1-source data 1. We compared the tumor purity between the LNM-positive (with average 87.75%) and negative patients (with average 88.27%). The result showed there was no difference between the two groups (P = 0.46, Student’s t-test), demonstrating the high purity and quality of the tumor tissues. (Figure1-supplementary figure 1J in the revision).

These results indicate that, in our study the differences between LNM-positive and LNM-negative groups are mainly caused by tumor tissues. However, the tumor microenvironment may also play a critical but not direct role in T1 CRC development and progression.

Figure RL1. A. Comparison of xCell scores of immune and microenvironment between the LNM-negative group (n= 143) and LNM-positive group (n= 78). B&C. Immune/stromal signatures identified from xCell, together with derived relative abundance of immune and stromal cell types. D, E, F. Identified signature proteins (D), LNM-positive group up-regulated proteins (E) and LNM-negative group up-regulated proteins (F) were mostly validated by HPA IHC Staining Data. G. Barplot for tumor purity between LNM-negative and -positive patients.

5) Contextualize the results:

According to the reviewer’s advice, we have made corresponding adjustments in the revised manuscript, for example:

• “We have made a comprehensive proteomic study of T1 CRC and provides a reliable data source for future research. “(line 342, page 17 in the revision)

-“Here, we present a comprehensive proteomic study to focus on LNM in patients with submucosal T1 CRCs.” (line 788, page 37 in the revision)

With regard to the problem of results are reported without context, we have provided supplementary descriptions of the context of the results in the “Result” section of the revised manuscript, for example:

• “Mucinous adenocarcinoma was considered to be a significant risk factor of LNM in T1 CRC (PMID: 31620912).” (line 498, page 24 in the revision)

• “Mucinous adenocarcinoma of the colorectal is a lethal cancer with unknown molecular etiology and a high propensity to lymph node metastasis. Previous proteomic studies on mucinous adenocarcinoma have found the proteins associated with treatment response in rectal mucinous adenocarcinoma and mechanisms of metastases in mucinous salivary adenocarcinoma.” (PMID: 34990823, 28249646) (line 534-538, page 26 in the revision)

• “Previous studies have shown that PDPN expression correlated with LNM in numerous cancers, especially in early oral squamous cell carcinomas.” (PMID: 21105028).” (line 570, page 27 in the revision)

6) Multivariate analysis of RHOT2:

RHOT2 and its paralog RHOT1 plays an important role in mitochondrial trafficking (PMID: 16630562). Although the function of RHOT2 in cancer is still unknown, the expression of RHOT1 affects metastasis in a variety of tumors, including pancreatic cancer (PMID: 26101710), gastric cancer (PMID: 35170374), small cell lung cancer (PMID: 33515563), etc. In addition, previous studies have found that Myc regulation of mitochondrial trafficking through RHOT1 and RHOT2 enables tumor cell motility and metastasis (PMID: 31061095).

As shown in Figure 4, in our analysis of previous version, we found RHOT2 was significant down-regulated (Log2FC=-1.35; p=0.003, Wilcoxon rank-sum test) in LNM-positive patients compared with LNM-negative patients in our T1 CRC cohort and the low level of RHOT2 is related to low overall survival of patients with colon cancer in TCGA cohort. Knockdown of RHOT2 expression could markedly enhance the migration ability of colon cancer cells.

In order to further explore the influence of RHOT2 on T1 CRC LNM, in addition to the previous results, we carried out the following analysis as shown in Figure4 in the revision.

We, firstly, calculated the correlations between the expression of RHOT2 and other proteins in our cohort (Figure 4). 1,508 proteins were correlated significantly (P < 0.05, Spearman) with RHOT2, and 1,354 proteins showed a positive correlation (coefficient >0) with RHOT2, and 154 proteins were negatively correlated with RHOT2 (coefficient <0). However, when we performed GSEA in RHOT2-associated proteins to identify biological signatures impacted by RHOT2, most of the obtained pathways (p<0.01) showed NES less than 0, which means these pathways were mainly enriched in RHOT2-negative-correlated group, only “mitochondrion” (GOCC) had a positive correlation (Figure 4). As we known RHOT2 is an important protein involved in the regulation of mitochondrial dynamics and mitophagy (PMID: 16630562). This result indicates that the involvement of RHOT2 in regulation of mitochondrial function might contribute to the pathogenesis of metastasis in cancer, especially in early-stage CRC. Consistent with the previous results, RHOT2-negative-correlated group was significantly enriched for EMT (HALLMARK) and complement and coagulation cascades pathways. Proteins up-regulated in LNM-positive group (LNM+ vs. LNM-: Log2FC >0; p<0.05, Wilcoxon rank-sum test) were negatively correlated with RHOT2(p < 0.05, coefficient<0, Spearman), including CAP2, COL6A3, COL6A2, TNC, DPYSL3, PCOLCE and BGN in pathway EMT; and GUCY1B3, VWF and F13A1 in pathway complement and coagulation cascades (Figure 2E, L; Figure 4D in the revision). ECM, focal adhesion and Dilated cardiomyopathy (DCM) pathways were also enriched in negative-correlated group. Degradation of RHOT2 has already been reported to be associated with DCM (PMID: 31455181). Overall, combined with the previous results, RHOT2 may play an important role in T1 CRC LNM (Figure 4D in the revision.).

As reviewer mentioned the data on RHOT2 are promising, but the understanding of it is preliminary. More analytical studies and experiments are needed in our future researches to understand the specific role and mechanism of RHOT2 in the process of tumor metastasis. In the revision, we discussed these limitations of our research.

Author Response

Reviewer #1 (Public Review):

The central claim that the R400Q mutation causes cardiomyopathy in humans require(s) additional support.

We regret that the reviewer interpreted our conclusions as described. Because of the extreme rarity of the MFN2 R400Q mutation our clinical data are unavoidably limited and therefore insufficient to support a conclusion that it causes cardiomyopathy “in humans”. Importantly, this is a claim that we did not make and do not believe to be the case. Our data establish that the MFN2 R400Q mutation is sufficient to cause lethal cardiomyopathy in some mice (Q/Q400a; Figure 4) and predisposes to doxorubicin-induced cardiomyopathy in the survivors (Q/Q400n; new data, Figure 7). Based on the clinical association we propose that R400Q may act as a genetic risk modifier in human cardiomyopathy.

To avoid further confusion we modified the manuscript title to “A human mitofusin 2 mutation can cause mitophagic cardiomyopathy” and provide a more detailed discussion of the implications and limitations of our study on page 11).

First, the claim of an association between the R400Q variant (identified in three individuals) and cardiomyopathy has some limitations based on the data presented. The initial association is suggested by comparing the frequency of the mutation in three small cohorts to that in a large database gnomAD, which aggregates whole exome and whole genome data from many other studies including those from specific disease populations. Having a matched control population is critical in these association studies.

We have added genotyping data from the matched non-affected control population (n=861) of the Cincinnati Heart study to our analyses (page 4). The conclusions did not change.

For instance, according to gnomAD the MFN2 Q400P variant, while not observed in those of European ancestry, has a 10-fold higher frequency in the African/African American and South Asian populations (0.0004004 and 0.0003266, respectively). If the authors data in table one is compared to the gnomAD African/African American population the p-value drops to 0.029262, which would not likely survive correction for multiple comparison (e.g., Bonferroni).

Thank you for raising the important issue of racial differences in mutant allele prevalence and its association with cardiomyopathy. Sample size for this type of sub-group analysis is limited, but we are able to provide African-derived population allele frequency comparisons for both the gnomAD population and our own non-affected control group.

As now described on page 4, and just as with the gnomAD population we did not observe MFN2 R400Q in any Caucasian individuals, either cardiomyopathy or control. Its (heterozygous only) prevalence in African American cardiomyopathy is 3/674. Thus, the R400Q minor allele frequency of 3/1,345 in AA cardiomyopathy compares to 10/24,962 in African gnomAD, reflecting a statistically significant increase in this specific population group (p=0.003308; Chi2 statistic 8.6293). Moreover, all African American non-affected controls in the case-control cohort were wild-type for MFN2 (0/452 minor alleles).

(The source and characteristics of the subjects used by the authors in Table 1 is not clear from the methods.)

The details of our study cohorts were inadvertently omitted during manuscript preparation. As now reported on pages 3 and 4, the Cincinnati Heart Study is a case-control study consisting of 1,745 cardiomyopathy (1,117 Caucasian and 628 African American) subjects and 861 non-affected controls (625 Caucasian and 236 African American) (Liggett et al Nat Med 2008; Matkovich et al JCI 2010; Cappola et al PNAS 2011). The Houston hypertrophic cardiomyopathy cohort [which has been screened by linkage analysis, candidate gene sequencing or clinical genetic testing) included 286 subjects (240 Caucasians and 46 African Americans) (Osio A et al Circ Res 2007; Li L et al Circ Res 2017).

Relatedly, evaluation in a knock-in mouse model is offered as a way of bolstering the claim for an association with cardiomyopathy. Some caution should be offered here. Certain mutations have caused a cardiomyopathy in mice when knocked in have not been observed in humans with the same mutation. A recent example is the p.S59L variant in the mitochondrial protein CHCHD10, which causes cardiomyopathy in mice but not in humans (PMID: 30874923). While phenocopy is suggestive there are differences in humans and mice, which makes the correlation imperfect.

We understand that a mouse is not a man, and as noted above we view the in vitro data in multiple cell systems and the in vivo data in knock-in mice as supportive for, not proof of, the concept that MFN2 R400Q can be a genetic cardiomyopathy risk modifier. As indicated in the following responses, we have further strengthened the case by including results from 2 additional, previously undescribed human MFN2 mutation knock-in mice.

Additionally, the argument that the Mfn2 R400Q variant causes a dominant cardiomyopathy in humans would be better supported by observing of a cardiomyopathy in the heterozygous Mfn2 R400Q mice and not just in the homozygous Mfn2 R400Q mice.

We are intrigued that in the previous comment the reviewer warns that murine phenocopies are not 100% predictive of human disease, and in the next sentence he/she requests that we show that the gene dose-phenotype response is the same in mice and humans. And, we again wish to note that we never argued that MFN2 R400Q “causes a dominant cardiomyopathy in humans.” Nevertheless, we understand the underlying concerns and in the revised manuscript we present data from new doxorubicin challenge experiments comparing cardiomyopathy development and myocardial mitophagy in WT, heterozygous, and surviving (Q/Q400n) homozygous Mfn2 R400Q KI mice (new Figure 7, panels E-G). Homozygous, but not heterozygous, R400Q mice exhibited an amplified cardiomyopathic response (greater LV dilatation, reduced LV ejection performance, exaggerated LV hypertrophy) and an impaired myocardial mitophagic response to doxorubicin. These in vivo data recapitulate new in vitro results in H9c2 rat cardiomyoblasts expressing MFN2 R400Q, which exhibited enhanced cytotoxicity (cell death and TUNEL labelling) to doxorubicin associated with reduced reactive mitophagy (Parkin aggregation and mitolysosome formation) (new Figure 7, panels A-D). Thus, under the limited conditions we have explored to date we do not observe cardiomyopathy development in heterozygous Mfn2 R400Q KI mice. However, we have expanded the association between R400Q, mitophagy and cardiomyopathy thereby providing the desired additional support for our argument that it can be a cardiomyopathy risk modifier.

Relatedly, it is not clear what the studies in the KI mouse prove over what was already known. Mfn2 function is known to be essential during the neonatal period and the authors have previously shown that the Mfn2 R400Q disrupts the ability of Mfn2 to mediate mitochondrial fusion, which is its core function. The results in the KI mouse seem consistent with those two observations, but it's not clear how they allow further conclusions to be drawn.

We strenuously disagree with the underlying proposition of this comment, which is that “mitochondrial fusion (is the) core function” of mitofusins. We also believe that our previous work, alluded to but not specified, is mischaracterized.

Our seminal study defining an essential role for Mfn2 for perinatal cardiac development (Gong et al Science 2015) reported that an engineered MFN2 mutation that was fully functional for mitochondrial fusion, but incapable of binding Parkin (MFN2 AA), caused perinatal cardiomyopathy when expressed as a transgene. By contrast, another engineered MFN2 mutant transgene that potently suppressed mitochondrial fusion, but constitutively bound Parkin (MFN2 EE) had no adverse effects on the heart.

Our initial description of MFN2 R400Q and observation that it exhibited impaired fusogenicity (Eschenbacher et al PLoS One 2012) reported results of in vitro studies and transgene overexpression in Drosophila. Importantly, a role for MFN2 in mitophagy was unknown at that time and so was not explored.

A major point both of this manuscript and our work over the last decade on mitofusin proteins has been that their biological importance extends far beyond mitochondrial fusion. As introduced/discussed throughout our manuscript, MFN2 plays important roles in mitophagy and mitochondrial motility. Because this central point seems to have been overlooked, we have gone to great lengths in the revised manuscript to unambiguously show that impaired mitochondrial fusion is not the critical functional aspect that determines disease phenotypes caused by Mfn2 mutations. To accomplish this we’ve re-structured the experiments so that R400Q is compared at every level to two other natural MFN2 mutations linked to a human disease, the peripheral neuropathy CMT2A. These comparators are MFN2 T105M in the GTPase domain and MFN2 M376A/V in the same HR1 domain as MFN2 R400Q. Each of these human MFN2 mutations is fusion-impaired, but the current studies reveal that that their spectrum of dysfunction differs in other ways as summarized in Author response table 1:

Author response table 1.

We understand that it sounds counterintuitive for a mutation in a “mitofusin” protein to evoke cardiac disease independent of its appellative function, mitochondrial fusion. But the KI mouse data clearly relate the occurrence of cardiomyopathy in R400Q mice to the unique mitophagy defect provoked in vitro and in vivo by this mutation. We hope the reviewer will agree that the KI models provide fresh scientific insight.

Additionally, the authors conclude that the effect of R400Q on the transcriptome and metabolome in a subset of animals cannot be explained by its effect on OXPHOS (based on the findings in Figure 4H). However, an alternative explanation is that the R400Q is a loss of function variant but does not act in a dominant negative fashion. According to this view, mice homozygous for R400Q (and have no wildtype copies of Mfn2) lack Mfn2 function and consequently have an OXPHOS defect giving rise to the observed transcriptomic and metabolomic changes. But in the rat heart cell line with endogenous rat Mfn2, exogenous of the MFN2 R400Q has no effect as it is loss of function and is not dominant negative.

Our results in the original submission, which are retained in Figures 1D and 1E and Figure 1 Figure Supplement 1 of the revision, exclude the possibility that R400Q is a functional null mutant for, but not a dominant suppressor of, mitochondrial fusion. We have added additional data for M376A in the revision, but the original results are retained in the main figure panels and a new supplemental figure:

Figure 1D reports results of mitochondrial elongation studies (the morphological surrogate for mitochondrial fusion) performed in Mfn1/Mfn2 double knock-out (DKO) MEFs. The baseline mitochondrial aspect ratio in DKO cells infected with control (b-gal containing) virus is ~2 (white bar), and increases to ~6 (i.e. ~normal) by forced expression of WT MFN2 (black bar). By contrast, aspect ratio in DKO MEFs expressing MFN2 mutants T105M (green bar), M376A and R400Q (red bars in main figure), R94Q and K109A (green bars in the supplemental figure) is only 3-4. For these results the reviewer’s and our interpretation agree: all of the MFN2 mutants studied are non-functional as mitochondrial fusion proteins.

Importantly, Figure 1E (left panel) reports the results of parallel mitochondrial elongation studies performed in WT MEFs, i.e. in the presence of normal endogenous Mfn1 and Mfn2. Here, baseline mitochondrial aspect ratio is already normal (~6, white bar), and increases modestly to ~8 when WT MFN2 is expressed (black bar). By comparison, aspect ratio is reduced below baseline by expression of four of the five MFN2 mutants, including MFN2 R400Q (main figure and accompanying supplemental figure; green and red bars). Only MFN2 M376A failed to suppress mitochondrial fusion promoted by endogenous Mfns 1 and 2. Thus, MFN2 R400Q dominantly suppresses mitochondrial fusion. We have stressed this point in the text on page 5, first complete paragraph.

Additionally, as the authors have shown MFN2 R400Q loses its ability to promote mitochondrial fusion, and this is the central function of MFN2, it is not clear why this can't be the explanation for the mouse phenotype rather than the mitophagy mechanism the authors propose.

Please see our response #7 above beginning “We strenuously disagree...”

Finally, it is asserted that the MFN2 R400Q variant disrupts Parkin activation, by interfering with MFN2 acting a receptor for Parkin. The support for this in cell culture however is limited. Additionally, there is no assessment of mitophagy in the hearts of the KI mouse model.

The reviewer may have overlooked the studies reported in original Figure 5, in which Parkin localization to cultured cardiomyoblast mitochondria is linked both to mitochondrial autophagy (LC3-mitochondria overlay) and to formation of mito-lysosomes (MitoQC staining). These results have been retained and expanded to include MFN2 M376A in Figure 6 B-E and Figure 6 Figure Supplement 1 of the revised manuscript. Additionally, selective impairment of Parkin recruitment to mitochondria was shown in mitofusin null MEFs in current Figure 3C and Figure 3 Figure Supplement 1, panels B and C.

The in vitro and in vivo doxorubicin studies performed for the revision further strengthen the mechanistic link between cardiomyocyte toxicity, reduced parkin recruitment and impaired mitophagy in MFN2 R400Q expressing cardiac cells: MFN2 R400Q-amplified doxorubicin-induced H9c2 cell death is associated with reduced Parkin aggregation and mitolysosome formation in vitro, and the exaggerated doxorubicin-induced cardiomyopathic response in MFN2 Q/Q400 mice was associated with reduced cardiomyocyte mitophagy in vivo, measured with adenoviral Mito-QC (new Figure 7).

Reviewer #2 (Public Review):

In this manuscript, Franco et al show that the mitofusin 2 mutation MFN2 Q400 impaires mitochondrial fusion with normal GTPase activity. MFN2 Q400 fails to recruit Parkin and further disrupts Parkin-mediated mitophagy in cultured cardiac cells. They also generated MFN2 Q400 knock-in mice to show the development of lethal perinatal cardiomyopathy, which had an impairment in multiple metabolic pathways.

The major strength of this manuscript is the in vitro study that provides a thorough understanding in the characteristics of the MFN2 Q400 mutant in function of MFN2, and the effect on mitochondrial function. However, the in vivo MFN2 Q/Q400 knock-in mice are more troubling given the split phenotype of MFN2 Q/Q400a vs MFN2 Q/Q400n subtypes. Their main findings towards impaired metabolism in mutant hearts fail to distinguish between the two subtypes.

Thanks for the comments. We do not fully understand the statement that “impaired metabolism in mutant hearts fails to distinguish between the two (in vivo) subtypes.” The data in current Figure 5 and its accompanying figure supplements show that impaired metabolism measured both as metabolomic and transcriptomic changes in the subtypes (orange Q400n vs red Q400a in Figure 5 panels A and D) are reflected in the histopathological analyses. Moreover, newly presented data on ROS-modifying pathways (Figure 5C) suggest that a central difference between Mfn2 Q/Q400 hearts that can compensate for the underlying impairment in mitophagic quality control (Q400n) vs those that cannot (Q400a) is the capacity to manage downstream ROS effects of metabolic derangements and mitochondrial uncoupling. Additional support for this idea is provided in the newly performed doxorubicin challenge experiments (Figure 7), demonstrating that mitochondrial ROS levels are in fact increased at baseline in adult Q400n mice.

While the data support the conclusion that MFN2 Q400 causes cardiomyopathy, several experiments are needed to further understand mechanism.

We thank the reviewer for agreeing with our conclusion that MFN2 Q400 can cause cardiomyopathy, which was the major issue raised by R1. As detailed below we have performed a great deal of additional experimentation, including on two completely novel MFN2 mutant knock-in mouse models, to validate the underlying mechanism.

This manuscript will likely impact the field of MFN2 mutation-related diseases and show how MFN2 mutation leads to perinatal cardiomyopathy in support of previous literature.

Thank you again. We think our findings have relevance beyond the field of MFN2 mutant-related disease as they provide the first evidence (to our knowledge) that a naturally occurring primary defect in mitophagy can manifest as myocardial disease.

Author Response

Reviewer #1 (Public Review):

This work introduces a novel framework for evaluating the performance of statistical methods that identify replay events. This is challenging because hippocampal replay is a latent cognitive process, where the ground truth is inaccessible, so methods cannot be evaluated against a known answer. The framework consists of two elements:

1) A replay sequence p-value, evaluated against shuffled permutations of the data, such as radon line fitting, rank-order correlation, or weighted correlation. This element determines how trajectory-like the spiking representation is. The p-value threshold for all accepted replay events is adjusted based on an empirical shuffled distribution to control for the false discovery rate.

2) A trajectory discriminability score, also evaluated against shuffled permutations of the data. In this case, there are two different possible spatial environments that can be replayed, so the method compares the log odds of track 1 vs. track 2.

The authors then use this framework (accepted number of replay events and trajectory discriminability) to study the performance of replay identification methods. They conclude that sharp wave ripple power is not a necessary criterion for identifying replay event candidates during awake run behavior if you have high multiunit activity, a higher number of permutations is better for identifying replay events, linear Bayesian decoding methods outperform rank-order correlation, and there is no evidence for pre-play.

The authors tackle a difficult and important problem for those studying hippocampal replay (and indeed all latent cognitive processes in the brain) with spiking data: how do we understand how well our methods are doing when the ground truth is inaccessible? Additionally, systematically studying how the variety of methods for identifying replay perform, is important for understanding the sometimes contradictory conclusions from replay papers. It helps consolidate the field around particular methods, leading to better reproducibility in the future. The authors' framework is also simple to implement and understand and the code has been provided, making it accessible to other neuroscientists. Testing for track discriminability, as well as the sequentiality of the replay event, is a sensible additional data point to eliminate "spurious" replay events.

However, there are some concerns with the framework as well. The novelty of the framework is questionable as it consists of a log odds measure previously used in two prior papers (Carey et al. 2019 and the authors' own Tirole & Huelin Gorriz, et al., 2022) and a multiple comparisons correction, albeit a unique empirical multiple comparisons correction based on shuffled data.

With respect to the log odds measure itself, as presented, it is reliant on having only two options to test between, limiting its general applicability. Even in the data used for the paper, there are sometimes three tracks, which could influence the conclusions of the paper about the validity of replay methods. This also highlights a weakness of the method in that it assumes that the true model (spatial track environment) is present in the set of options being tested. Furthermore, the log odds measure itself is sensitive to the defined ripple or multiunit start and end times, because it marginalizes over both position and time, so any inclusion of place cells that fire for the animal's stationary position could influence the discriminability of the track. Multiple track representations during a candidate replay event would also limit track discriminability. Finally, the authors call this measure "trajectory discriminability", which seems a misnomer as the time and position information are integrated out, so there is no notion of trajectory.

The authors also fail to make the connection with the control of the false discovery rate via false positives on empirical shuffles with existing multiple comparison corrections that control for false discovery rates (such as the Benjamini and Hochberg procedure or Storey's q-value). Additionally, the particular type of shuffle used will influence the empirically determined p-value, making the procedure dependent on the defined null distribution. Shuffling the data is also considerably more computationally intensive than the existing multiple comparison corrections.

Overall, the authors make interesting conclusions with respect to hippocampal replay methods, but the utility of the method is limited in scope because of its reliance on having exactly two comparisons and having to specify the null distribution to control for the false discovery rate. This work will be of interest to electrophysiologists studying hippocampal replay in spiking data.

We would like to thank the reviewer for the feedback.

Firstly, we would like to clarify that it is not our intention to present this tool as a novel replay detection approach. It is indeed merely a novel tool for evaluating different replay detection methods. Also, while we previously used log odds metrics to quantify contextual discriminability within replay events (Tirole et al., 2021), this framework is novel in how it is used (to compare replay detection methods), and the use of empirically determined FPR-matched alpha levels. We have now modified the manuscript to make this point more explicit.

Our use of the term trajectory-discriminability is now changed to track-discriminability in the revised manuscript, given we are summing over time and space, as correctly pointed out by the reviewer.

While this approach requires two tracks in its current implementation, we have also been able to apply this approach to three tracks, with a minor variation in the method, however this is beyond the scope of our current manuscript. Prior experience on other tracks not analysed in the log odds calculation should not pose any issue, given that the animal likely replays many experiences of the day (e.g. the homecage). These “other” replay events likely contribute to candidate replay events that fail to have a statistically significant replay score on either track.

With regard to using a cell-id randomized dataset to empirically estimate false-positive rates, we have provided a detailed explanation behind our choice of using an alpha level correction in our response to the essential revisions above. This approach is not used to examine the effect of multiple comparisons, but rather to measure the replay detection error due to non-independence and a non-uniform p value distribution. Therefore we do not believe that existing multiple comparison corrections such as Benjamini and Hochberg procedure are applicable here (Author response image 1-3). Given the potential issues raised with a session-based cell-id randomization, we demonstrate above that the null distribution is sufficiently independent from the four shuffle-types used for replay detection (the same was not true for a place field randomized dataset) (Author response image 4).

Author response image 1.

Distribution of Spearman’s rank order correlation score and p value for false events with random sequence where each neuron fires one (left), two (middle) or three (right) spikes.

Author response image 2.

Distribution of Spearman’s rank order correlation score and p value for mixture of 20% true events and 80% false events where each neuron fires one (left), two (middle) or three (right) spikes.

Author response image 3.

Number of true events (blue) and false events (yellow) detected based on alpha level 0.05 (upper left), empirical false positive rate 5% (upper right) and false discovery rate 5% (lower left, based on BH method)

Author response image 4.

Proportion of false events detected when using dataset with within and cross experiment cell-id randomization and place field randomization. The detection was based on single shuffle including time bin permutation shuffle, spike train circular shift shuffle, place field circular shift shuffle, and place bin circular shift shuffle.

Reviewer #2 (Public Review):

This study proposes to evaluate and compare different replay methods in the absence of "ground truth" using data from hippocampal recordings of rodents that were exposed to two different tracks on the same day. The study proposes to leverage the potential of Bayesian methods to decode replay and reactivation in the same events. They find that events that pass a higher threshold for replay typically yield a higher measure of reactivation. On the other hand, events from the shuffled data that pass thresholds for replay typically don't show any reactivation. While well-intentioned, I think the result is highly problematic and poorly conceived.

The work presents a lot of confusion about the nature of null hypothesis testing and the meaning of p-values. The prescription arrived at, to correct p-values by putting animals on two separate tracks and calculating a "sequence-less" measure of reactivation are impractical from an experimental point of view, and unsupportable from a statistical point of view. Much of the observations are presented as solutions for the field, but are in fact highly dependent on distinct features of the dataset at hand. The most interesting observation is that despite the existence of apparent sequences in the PRE-RUN data, no reactivation is detectable in those events, suggesting that in fact they represent spurious events. I would recommend the authors focus on this important observation and abandon the rest of the work, as it has the potential to further befuddle and promote poor statistical practices in the field.

The major issue is that the manuscript conveys much confusion about the nature of hypothesis testing and the meaning of p-values. It's worth stating here the definition of a p-value: the conditional probability of rejecting the null hypothesis given that the null hypothesis is true. Unfortunately, in places, this study appears to confound the meaning of the p-value with the probability of rejecting the null hypothesis given that the null hypothesis is NOT true-i.e. in their recordings from awake replay on different mazes. Most of their analysis is based on the observation that events that have higher reactivation scores, as reflected in the mean log odds differences, have lower p-values resulting from their replay analyses. Shuffled data, in contrast, does not show any reactivation but can still show spurious replays depending on the shuffle procedure used to create the surrogate dataset. The authors suggest using this to test different practices in replay detection. However, another important point that seems lost in this study is that the surrogate dataset that is contrasted with the actual data depends very specifically on the null hypothesis that is being tested. That is to say, each different shuffle procedure is in fact testing a different null hypothesis. Unfortunately, most studies, including this one, are not very explicit about which null hypothesis is being tested with a given resampling method, but the p-value obtained is only meaningful insofar as the null that is being tested and related assumptions are clearly understood. From a statistical point of view, it makes no sense to adjust the p-value obtained by one shuffle procedure according to the p-value obtained by a different shuffle procedure, which is what this study inappropriately proposes. Other prescriptions offered by the study are highly dataset and method dependent and discuss minutiae of event detection, such as whether or not to require power in the ripple frequency band.

We would like to thank the reviewer for their feedback. The purpose of this paper is to present a novel tool for evaluating replay sequence detection using an independent measure that does not depend on the sequence score. As the reviewer stated, in this study, we are detecting replay events based on a set alpha threshold (0.05), based on the conditional probability of rejecting the null hypothesis given that the null hypothesis is true. For all replay events detected during PRE, RUN or POST, they are classified as track 1 or track 2 replay events by comparing each event’s sequence score relative to the shuffled distribution. Then, the log odds measure was only applied to track 1 and track 2 replay events selected using sequence-based detection. Its important to clarify that we never use log odds to select events to examine their sequenceness p value. Therefore, we disagree with the reviewer’s claim that for awake replay events detected on different tracks, we are quantifying the probability of rejecting the null hypothesis given that the null hypothesis is not true.

However, we fully understand the reviewer’s concerns with a cell-id randomization, and the potential caveats associated with using this approach for quantifying the false positive rate. First of all, we would like to clarify that the purpose of alpha level adjustment was to facilitate comparison across methods by finding the alpha level with matching false-positive rates determined empirically. Without doing this, it is impossible to compare two methods that differ in strictness (e.g. is using two different shuffles needed compared to using a single shuffle procedure). This means we are interested in comparing the performance of different methods at the equivalent alpha level where each method detects 5% spurious events per track rather than an arbitrary alpha level of 0.05 (which is difficult to interpret if statistical tests are run on non-independent samples). Once the false positive rate is matched, it is possible to compare two methods to see which one yields more events and/or has better track discriminability.

We agree with the reviewer that the choice of data randomization is crucial. When a null distribution of a randomized dataset is very similar to the null distribution used for detection, this should lead to a 5% false positive rate (as a consequence of circular reasoning). In our response to the essential revisions, we have discussed about the effect of data randomization on replay detection. We observed that while place field circularly shifted dataset and cell-id randomized dataset led to similar false-positive rates when shuffles that disrupt temporal information were used for detection, a place field circularly shifted dataset but not a cell-id randomized dataset was sensitive to shuffle methods that disrupted place information (Author response image 4). We would also like to highlight one of our findings from the manuscript that the discrepancy between different methods can be substantially reduced when alpha level was adjusted to match false-positive rates (Figure 6B). This result directly supports the utility of a cell-id randomized dataset in finding the alpha level with equivalent false positive rates across methods. Hence, while imperfect, we argue cell-id randomization remains an acceptable method as it is sufficiently different from the four shuffles we used for replay detection compared to place field randomized dataset (Author response image 4).

While the use of two linear tracks was crucial for our current framework to calculate log odds for evaluating replay detection, we acknowledge that it limits the applicability of this framework. At the same time, the conclusions of the manuscript with regard to ripples, replay methods, and preplay should remain valid on a single track. A second track just provides a useful control for how place cells can realistically remap within another environment. However, with modification, it may be applied to a maze with different arms or subregions, although this is beyond the scope of our current study.

Last of not least, we partly agree with the reviewer that the result can be dataset-specific such that the result may vary depending on animal’s behavioural state and experimental design. However, our results highlight the fact that there is a very wide distribution of both the track discriminability and the proportion of significant events detected across methods that are currently used in the field. And while we see several methods that appear comparable in their effectiveness in replay detection, there are also other methods that are deeply flawed (that have been previously been used in peer-reviewed publications) if the alpha level is not sufficiently strict. Regardless of the method used, most methods can be corrected with an appropriate alpha level (e.g. using all spikes for a rank order correlation). Therefore, while the exact result may be dataset-specific, we feel that this is most likely due to the number of cells and properties of the track more than the use of two tracks. Reporting of the empirically determined false-positive rate and use of alpha level with matching false-positive rate (such as 0.05) for detection does not require a second track, and the adoption of this approach by other labs would help to improve the interpretability and generalizability of their replay data.

Reviewer #3 (Public Review):

This study tackles a major problem with replay detection, which is that different methods can produce vastly different results. It provides compelling evidence that the source of this inconsistency is that biological data often violates assumptions of independent samples. This results in false positive rates that can vary greatly with the precise statistical assumptions of the chosen replay measure, the detection parameters, and the dataset itself. To address this issue, the authors propose to empirically estimate the false positive rate and control for it by adjusting the significance threshold. Remarkably, this reconciles the differences in replay detection methods, as the results of all the replay methods tested converge quite well (see Figure 6B). This suggests that by controlling for the false positive rate, one can get an accurate estimate of replay with any of the standard methods.

When comparing different replay detection methods, the authors use a sequence-independent log-odds difference score as a validation tool and an indirect measure of replay quality. This takes advantage of the two-track design of the experimental data, and its use here relies on the assumption that a true replay event would be associated with good (discriminable) reactivation of the environment that is being replayed. The other way replay "quality" is estimated is by the number of replay events detected once the false positive rate is taken into account. In this scheme, "better" replay is in the top right corner of Figure 6B: many detected events associated with congruent reactivation.

There are two possible ways the results from this study can be integrated into future replay research. The first, simpler, way is to take note of the empirically estimated false positive rates reported here and simply avoid the methods that result in high false positive rates (weighted correlation with a place bin shuffle or all-spike Spearman correlation with a spike-id shuffle). The second, perhaps more desirable, way is to integrate the practice of estimating the false positive rate when scoring replay and to take it into account. This is very powerful as it can be applied to any replay method with any choice of parameters and get an accurate estimate of replay.

How does one estimate the false positive rate in their dataset? The authors propose to use a cell-ID shuffle, which preserves all the firing statistics of replay events (bursts of spikes by the same cell, multi-unit fluctuations, etc.) but randomly swaps the cells' place fields, and to repeat the replay detection on this surrogate randomized dataset. Of course, there is no perfect shuffle, and it is possible that a surrogate dataset based on this particular shuffle may result in one underestimating the true false positive rate if different cell types are present (e.g. place field statistics may differ between CA1 and CA3 cells, or deep vs. superficial CA1 cells, or place cells vs. non-place cells if inclusion criteria are not strict). Moreover, it is crucial that this validation shuffle be independent of any shuffling procedure used to determine replay itself (which may not always be the case, particularly for the pre-decoding place field circular shuffle used by some of the methods here) lest the true false-positive rate be underestimated. Once the false positive rate is estimated, there are different ways one may choose to control for it: adjusting the significance threshold as the current study proposes, or directly comparing the number of events detected in the original vs surrogate data. Either way, with these caveats in mind, controlling for the false positive rate to the best of our ability is a powerful approach that the field should integrate.

Which replay detection method performed the best? If one does not control for varying false positive rates, there are two methods that resulted in strikingly high (>15%) false positive rates: these were weighted correlation with a place bin shuffle and Spearman correlation (using all spikes) with a spike-id shuffle. However, after controlling for the false positive rate (Figure 6B) all methods largely agree, including those with initially high false positive rates. There is no clear "winner" method, because there is a lot of overlap in the confidence intervals, and there also are some additional reasons for not overly interpreting small differences in the observed results between methods. The confidence intervals are likely to underestimate the true variance in the data because the resampling procedure does not involve hierarchical statistics and thus fails to account for statistical dependencies on the session and animal level. Moreover, it is possible that methods that involve shuffles similar to the cross-validation shuffle ("wcorr 2 shuffles", "wcorr 3 shuffles" both use a pre-decoding place field circular shuffle, which is very similar to the pre-decoding place field swap used in the cross-validation procedure to estimate the false positive rate) may underestimate the false positive rate and therefore inflate adjusted p-value and the proportion of significant events. We should therefore not interpret small differences in the measured values between methods, and the only clear winner and the best way to score replay is using any method after taking the empirically estimated false positive rate into account.

The authors recommend excluding low-ripple power events in sleep, because no replay was observed in events with low (0-3 z-units) ripple power specifically in sleep, but that no ripple restriction is necessary for awake events. There are problems with this conclusion. First, ripple power is not the only way to detect sharp-wave ripples (the sharp wave is very informative in detecting awake events). Second, when talking about sequence quality in awake non-ripple data, it is imperative for one to exclude theta sequences. The authors' speed threshold of 5 cm/s is not sufficient to guarantee that no theta cycles contaminate the awake replay events. Third, a direct comparison of the results with and without exclusion is lacking (selecting for the lower ripple power events is not the same as not having a threshold), so it is unclear how crucial it is to exclude the minority of the sleep events outside of ripples. The decision of whether or not to select for ripples should depend on the particular study and experimental conditions that can affect this measure (electrode placement, brain state prevalence, noise levels, etc.).

Finally, the authors address a controversial topic of de-novo preplay. With replay detection corrected for the false positive rate, none of the detection methods produce evidence of preplay sequences nor sequenceless reactivation in the tested dataset. This presents compelling evidence in favour of the view that the sequence of place fields formed on a novel track cannot be predicted by the sequential structure found in pre-task sleep.

We would like to thank the reviewer for the positive and constructive feedback.

We agree with the reviewer that the conclusion about the effect of ripple power is dataset-specific and is not intended to be a one-size-fit-all recommendation for wider application. But it does raise a concern that individual studies should address. The criteria used for selecting candidate events will impact the overall fraction of detected events, and makes the comparison between studies using different methods more difficult. We have updated the manuscript to emphasize this point.

“These results emphasize that a ripple power threshold is not necessary for RUN replay events in our dataset but may still be beneficial, as long as it does not excessively eliminate too many good replay events with low ripple power. In other words, depending on the experimental design, it is possible that a stricter p-value with no ripple threshold can be used to detect more replay events than using a less strict p-value combined with a strict ripple power threshold. However, for POST replay events, a threshold at least in the range of a z-score of 3-5 is recommended based on our dataset, to reduce inclusion of false-positives within the pool of detected replay events.”

“We make six key observations: 1) A ripple power threshold may be more important for replay events during POST compared to RUN. For our dataset, the POST replay events with ripple power below a z-score of 3-5 were indistinguishable from spurious events. While the exact ripple z-score threshold to implement may differ depending on the experimental condition (e.g. electrode placement, behavioural paradigm, noise level and etc) and experimental aim, our findings highlight the benefit of using ripple power threshold for detecting replay during POST. 2) ”

Author Response

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

Reviewer #1 (Public Review):

The authors present a number of deep learning models to analyse the dynamics of epithelia. In this way they want to overcome the time-consuming manual analysis of such data and also remove a potential operator bias. Specifically, they set up models for identifying cell division events and cell division orientation. They apply these tools to the epithelium of the developing Drosophila pupal wing. They confirm a linear decrease of the division density with time and identify a burst of cell division after healing of a wound that they had induced earlier. These division events happen a characteristic time after and a characteristic distance away from the wound. These characteristic quantities depend on the size of the wound.

Strengths:

The methods developed in this work achieve the goals set by the authors and are a very helpful addition to the toolbox of developmental biologists. They could potentially be used on various developing epithelia. The evidence for the impact of wounds on cell division is compelling.

The methods presented in this work should prove to be very helpful for quantifying cell proliferation in epithelial tissues.

We thank the reviewer for the positive comments!

Reviewer #2 (Public Review):

In this manuscript, the authors propose a computational method based on deep convolutional neural networks (CNNs) to automatically detect cell divisions in two-dimensional fluorescence microscopy timelapse images. Three deep learning models are proposed to detect the timing of division, predict the division axis, and enhance cell boundary images to segment cells before and after division. Using this computational pipeline, the authors analyze the dynamics of cell divisions in the epithelium of the Drosophila pupal wing and find that a wound first induces a reduction in the frequency of division followed by a synchronised burst of cell divisions about 100 minutes after its induction.

Comments on revised version:

Regarding the Reviewer's 1 comment on the architecture details, I have now understood that the precise architecture (number/type of layers, activation functions, pooling operations, skip connections, upsampling choice...) might have remained relatively hidden to the authors themselves, as the U-net is built automatically by the fast.ai library from a given classical choice of encoder architecture (ResNet34 and ResNet101 here) to generate the decoder part and skip connections.

Regarding the Major point 1, I raised the question of the generalisation potential of the method. I do not think, for instance, that the optimal number of frames to use, nor the optimal choice of their time-shift with respect to the division time (t-n, t+m) (not systematically studied here) may be generic hyperparameters that can be directly transferred to another setting. This implies that the method proposed will necessarily require re-labeling, re-training and re-optimizing the hyperparameters which directly influence the network architecture for each new dataset imaged differently. This limits the generalisation of the method to other datasets, and this may be seen as in contrast to other tools developed in the field for other tasks such as cellpose for segmentation, which has proven a true potential for generalisation on various data modalities. I was hoping that the authors would try themselves testing the robustness of their method by re-imaging the same tissue with slightly different acquisition rate for instance, to give more weight to their work.

We thank the referee for the comments. Regarding this particular biological system, due to photobleaching over long imaging periods (and the availability of imaging systems during the project), we would have difficulty imaging at much higher rates than the 2 minute time frame we currently use. These limitations are true for many such systems, and it is rarely possible to rapidly image for long periods of time in real experiments. Given this upper limit in framerate, we could, in principle, sample this data at a lower framerate, by removing time points of the videos but this typically leads to worse results. With some pilot data, we have tried to use fewer time intervals for our analysis but they always gave worse results. We found we need to feed the maximum amount of information available into the model to get the best results (i.e. the fastest frame rate possible, given the data available). Our goal is to teach the neural net to identify dynamic space-time localised events from time lapse videos, in which the duration of an event is a key parameter. Our division events take 10 minutes or less to complete therefore we used 5 timepoints in the videos for the deep learning model. If we considered another system with dynamic events which have a duration T when we would use T/t timepoints where t is the minimum time interval (for our data t=2min). For example if we could image every minute we would use 10 timepoints. As discussed below, we do envision other users with different imaging setups and requirements may need to retrain the model for their own data and to help with this, we have now provided more detailed instructions how to do this (see later).

In this regard, and because the authors claimed to provide clear instructions on how to reuse their method or adapt it to a different context, I delved deeper into the code and, to my surprise, felt that we are far from the coding practice of what a well-documented and accessible tool should be.

To start with, one has to be relatively accustomed with Napari to understand how the plugin must be installed, as the only thing given is a pip install command (that could be typed in any terminal without installing the plugin for Napari, but has to be typed inside the Napari terminal, which is mentioned nowhere). Surprisingly, the plugin was not uploaded on Napari hub, nor on PyPI by the authors, so it is not searchable/findable directly, one has to go to the Github repository and install it manually. In that regard, no description was provided in the copy-pasted templated files associated to the napari hub, so exporting it to the hub would actually leave it undocumented.

We thank the referee for suggesting the example of (DeXtrusion, Villars et al. 2023). We have endeavoured to produce similarly-detailed documentation for our tools. We now have clear instructions for installation requiring only minimal coding knowledge, and we have provided a user manual for the napari plug-in. This includes information on each of the options for using the model and the outputs they will produce. The plugin has been tested by several colleagues using both Windows and Mac operating systems.

Author response image 1.

Regarding now the python notebooks, one can fairly say that the "clear instructions" that were supposed to enlighten the code are really minimal. Only one notebook "trainingUNetCellDivision10.ipynb" has actually some comments, the other have (almost) none nor title to help the unskilled programmer delving into the script to guess what it should do. I doubt that a biologist who does not have a strong computational background will manage adapting the method to its own dataset (which seems to me unavoidable for the reasons mentioned above).

Within the README file, we have now included information on how to retrain the models with helpful links to deep learning tutorials (which, indeed, some of us have learnt from) for those new to deep learning. All Jupyter notebooks now include more comments explaining the models.

Finally regarding the data, none is shared publicly along with this manuscript/code, such that if one doesn't have a similar type of dataset - that must be first annotated in a similar manner - one cannot even test the networks/plugin for its own information. A common and necessary practice in the field - and possibly a longer lasting contribution of this work - could have been to provide the complete and annotated dataset that was used to train and test the artificial neural network. The basic reason is that a more performant, or more generalisable deep-learning model may be developed very soon after this one and for its performance to be fairly compared, it requires to be compared on the same dataset. Benchmarking and comparison of methods performance is at the core of computer vision and deep-learning.

We thank the referee for these comments. We have now uploaded all the data used to train the models and to test them, as well as all the data used in the analyses for the paper. This includes many videos that were not used for training but were analysed to generate the paper’s results. The link to these data sets is provided in our GitHub page (https://github.com/turleyjm/cell-division-dl- plugin/tree/main). In the folder for the data sets and in the GitHub repository, we have included the Jupyter notebooks used to train the models and these can be used for retraining. We have made our data publicly available at Zenodo dataset https://zenodo.org/records/10846684 (added to last paragraph of discussion). We have also included scripts that can be used to compare the model output with ground truth, including outputs highlighting false positives and false negatives. Together with these scripts, models can be compared and contrasted, both in general and in individual videos. Overall, we very much appreciate the reviewer’s advice, which has made the plugin much more user- friendly and, hopefully, easier for other groups to train their own models. Our contact details are provided, and we would be happy to advise any groups that would like to use our tools.

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

Reviewer #1 (Public Review):

The authors present a number of deep-learning models to analyse the dynamics of epithelia. In this way, they want to overcome the time-consuming manual analysis of such data and also remove a potential operator bias. Specifically, they set up models for identifying cell division events and cell division orientation. They apply these tools to the epithelium of the developing Drosophila pupal wing. They confirm a linear decrease of the division density with time and identify a burst of cell division after the healing of a wound that they had induced earlier. These division events happen a characteristic time after and a characteristic distance away from the wound. These characteristic quantities depend on the size of the wound.

Strength:

The methods developed in this work achieve the goals set by the authors and are a very helpful addition to the toolbox of developmental biologists. They could potentially be used on various developing epithelia. The evidence for the impact of wounds on cell division is solid.

Weakness:

Some aspects of the deep-learning models remained unclear, and the authors might want to think about adding details. First of all, for readers not being familiar with deep-learning models, I would like to see more information about ResNet and U-Net, which are at the base of the new deep-learning models developed here. What is the structure of these networks?

We agree with the Reviewer and have included additional information on page 8 of the manuscript, outlining some background information about the architecture of ResNet and U-Net models.

How many parameters do you use?

We apologise for this omission and have now included the number of parameters and layers in each model in the methods section on page 25.

What is the difference between validating and testing the model? Do the corresponding data sets differ fundamentally?

The difference between ‘validating’ and ‘testing’ the model is validating data is used during training to determine whether the model is overfitting. If the model is performing well on the training data but not on the validating data, this a key signal the model is overfitting and changes will need to be made to the network/training method to prevent this. The testing data is used after all the training has been completed and is used to test the performance of the model on fresh data it has not been trained on. We have removed refence to the validating data in the main text to make it simpler and add this explanation to the methods. There is no fundamental (or experimental) difference between each of the labelled data sets; rather, they are collected from different biological samples. We have now included this information in the Methods text on page 24.

How did you assess the quality of the training data classification?

These data were generated and hand-labelled by an expert with many years of experience in identifying cell divisions in imaging data, to give the ground truth for the deep learning model.

Reviewer #1 (Recommendations For The Authors):

You repeatedly use 'new', 'novel' as well as 'surprising' and 'unexpected'. The latter are rather subjective and it is not clear based on what prior knowledge you make these statements. Unless indicated otherwise, it is understood that the results and methods are new, so you can delete these terms.

We have deleted these words, as suggested, for almost all cases.

p.4 "as expected" add a reference or explain why it is expected.

A reference has now been included in this section, as suggested.

p.4 "cell divisions decrease linearly with time" Only later (p.10) it turns out that you think about the density of cell divisions.

This has been changed to "cell division density decreases linearly with time".

p.5 "imagine is largely in one plane" while below "we generated a 3D z-stack" and above "our in vivo 3D image data" (p.4). Although these statements are not strictly contradictory, I still find them confusing. Eventually, you analyse a 2D image, so I would suggest that you refer to your in vivo data as being 2D.

We apologise for the confusion here; the imaging data was initially generated using 3D z-stacks but this 3D data is later converted to a 2D focused image, on which the deep learning analysis is performed. We are now more careful with the language in the text.

p.7 "We have overcome (...) the standard U-Net model" This paragraph remains rather cryptic to me. Maybe you can explain in two sentences what a U-Net is or state its main characteristics. Is it important to state which class you have used at this point? Similarly, what is the exact role of the ResNet model? What are its characteristics?

We have included more details on both the ResNet and U-Net models and how our model incorporates properties from them on Page 8.

p.8 Table 1 Where do I find it? Similarly, I could not find Table 2.

These were originally located in the supplemental information document, but have been moved to the main manuscript.

p.9 "developing tissue in normal homeostatic conditions" Aren't homeostatic and developing contradictory? In one case you maintain a state, in the other, it changes.

We agree with the Reviewer and have removed the word ‘homeostatic’.

p.9 "Develop additional models" I think 'models' refers to deep learning models, not to physical models of epithelial tissue development. Maybe you can clarify this?

Yes, this is correct; we have phrased this better in the text.

p.12 "median error" median difference to the manually acquired data?

Yes, and we have made this clearer in the text, too.

p.12 "we expected to observe a bias of division orientation along this axis" Can you justify the expectation? Elongated cells are not necessarily aligned with the direction of a uniaxially applied stress.

Although this is not always the case, we have now included additional references to previous work from other groups which demonstrated that wing epithelial cells do become elongated along the P/D axis in response to tension.

p.14 "a rather random orientation" Please, quantify.

The division orientations are quantified in Fig. 4F,G; we have now changed our description from ‘random’ to ‘unbiased’.

p.17 "The theories that must be developed will be statistical mechanical (stochastic) in nature" I do not understand. Statistical mechanics refers to systems at thermodynamic equilibrium, stochastic to processes that depend on, well, stochastic input.

We have clarified that we are referring to non-equilibrium statistical mechanics (the study of macroscopic systems far from equilibrium, a rich field of research with many open problems and applications in biology).

Reviewer #2 (Public Review):

In this manuscript, the authors propose a computational method based on deep convolutional neural networks (CNNs) to automatically detect cell divisions in two-dimensional fluorescence microscopy timelapse images. Three deep learning models are proposed to detect the timing of division, predict the division axis, and enhance cell boundary images to segment cells before and after division. Using this computational pipeline, the authors analyze the dynamics of cell divisions in the epithelium of the Drosophila pupal wing and find that a wound first induces a reduction in the frequency of division followed by a synchronised burst of cell divisions about 100 minutes after its induction.

In general, novelty over previous work does not seem particularly important. From a methodological point of view, the models are based on generic architectures of convolutional neural networks, with minimal changes, and on ideas already explored in general. The authors seem to have missed much (most?) of the literature on the specific topic of detecting mitotic events in 2D timelapse images, which has been published in more specialized journals or Proceedings. (TPMAI, CCVPR etc., see references below). Even though the image modality or biological structure may be different (non-fluorescent images sometimes), I don't believe it makes a big difference. How the authors' approach compares to this previously published work is not discussed, which prevents me from objectively assessing the true contribution of this article from a methodological perspective.

On the contrary, some competing works have proposed methods based on newer - and generally more efficient - architectures specifically designed to model temporal sequences (Phan 2018, Kitrungrotsakul 2019, 2021, Mao 2019, Shi 2020). These natural candidates (recurrent networks, long-short-term memory (LSTM) gated recurrent units (GRU), or even more recently transformers), coupled to CNNs are not even mentioned in the manuscript, although they have proved their generic superiority for inference tasks involving time series (Major point 2). Even though the original idea/trick of exploiting the different channels of RGB images to address the temporal aspect might seem smart in the first place - as it reduces the task of changing/testing a new architecture to a minimum - I guess that CNNs trained this way may not generalize very well to videos where the temporal resolution is changed slightly (Major point 1). This could be quite problematic as each new dataset acquired with a different temporal resolution or temperature may require manual relabeling and retraining of the network. In this perspective, recent alternatives (Phan 2018, Gilad 2019) have proposed unsupervised approaches, which could largely reduce the need for manual labeling of datasets.

We thank the reviewer for their constructive comments. Our goal is to develop a cell detection method that has a very high accuracy, which is critical for practical and effective application to biological problems. The algorithms need to be robust enough to cope with the difficult experimental systems we are interested in studying, which involve densely packed epithelial cells within in vivo tissues that are continuously developing, as well as repairing. In response to the above comments of the reviewer, we apologise for not including these important papers from the division detection and deep learning literature, which are now discussed in the Introduction (on page 4).

A key novelty of our approach is the use of multiple fluorescent channels to increase information for the model. As the referee points out, our method benefits from using and adapting existing highly effective architectures. Hence, we have been able to incorporate deeper models than some others have previously used. An additional novelty is using this same model architecture (retrained) to detect cell division orientation. For future practical use by us and other biologists, the models can easily be adapted and retrained to suit experimental conditions, including different multiple fluorescent channels or number of time points. Unsupervised approaches are very appealing due to the potential time saved compared to manual hand labelling of data. However, the accuracy of unsupervised models are currently much lower than that of supervised (as shown in Phan 2018) and most importantly well below the levels needed for practical use analysing inherently variable (and challenging) in vivo experimental data.

Regarding the other convolutional neural networks described in the manuscript:

(1) The one proposed to predict the orientation of mitosis performs a regression task, predicting a probability for the division angle. The architecture, which must be different from a simple Unet, is not detailed anywhere, so the way it was designed is difficult to assess. It is unclear if it also performs mitosis detection, or if it is instead used to infer orientation once the timing and location of the division have been inferred by the previous network.

The neural network used for U-NetOrientation has the same architecture as U-NetCellDivision10 but has been retrained to complete a different task: finding division orientation. Our workflow is as follows: firstly, U-NetCellDivision10 is used to find cell divisions; secondly, U-NetOrientation is applied locally to determine the division orientation. These points have now been clarified in the main text on Page 14.

(2) The one proposed to improve the quality of cell boundary images before segmentation is nothing new, it has now become a classic step in segmentation, see for example Wolny et al. eLife 2020.

We have cited similar segmentation models in our paper and thank the referee for this additional one. We had made an improvement to the segmentation models, using GFP-tagged E-cadherin, a protein localised in a thin layer at the apical boundary of cells. So, while this is primarily a 2D segmentation problem, some additional information is available in the z-axis as the protein is visible in 2-3 separate z-slices. Hence, we supplied this 3-focal plane input to take advantage of the 3D nature of this signal. This approach has been made more explicit in the text (Pages 14, 15) and Figure (Fig. 2D).

As a side note, I found it a bit frustrating to realise that all the analysis was done in 2D while the original images are 3D z-stacks, so a lot of the 3D information had to be compressed and has not been used. A novelty, in my opinion, could have resided in the generalisation to 3D of the deep-learning approaches previously proposed in that context, which are exclusively 2D, in particular, to predict the orientation of the division.

Our experimental system is a relatively flat 2D tissue with the orientation of the cell divisions consistently in the xy-plane. Hence, a 2D analysis is most appropriate for this system. With the successful application of the 2D methods already achieving high accuracy, we envision that extension to 3D would only offer a slight increase in effectiveness as these measurements have little room for improvement. Therefore, we did not extend the method to 3D here. However, of course, this is the next natural step in our research as 3D models would be essential for studying 3D tissues; such 3D models will be computationally more expensive to analyse and more challenging to hand label.

Concerning the biological application of the proposed methods, I found the results interesting, showing the potential of such a method to automatise mitosis quantification for a particular biological question of interest, here wound healing. However, the deep learning methods/applications that are put forward as the central point of the manuscript are not particularly original.

We thank the referee for their constructive comments. Our aim was not only to show the accuracy of our models but also to show how they might be useful to biologists for automated analysis of large datasets, which is a—if not the—bottleneck for many imaging experiments. The ability to process large datasets will improve robustness of results, as well as allow additional hypotheses to be tested. Our study also demonstrated that these models can cope with real in vivo experiments where additional complications such as progressive development, tissue wounding and inflammation must be accounted for.

Major point 1: generalisation potential of the proposed method.

The neural network model proposed for mitosis detection relies on a 2D convolutional neural network (CNN), more specifically on the Unet architecture, which has become widespread for the analysis of biology and medical images. The strategy proposed here exploits the fact that the input of such an architecture is natively composed of several channels (originally 3 to handle the 3 RGB channels, which is actually a holdover from computer vision, since most medical/biological images are gray images with a single channel), to directly feed the network with 3 successive images of a timelapse at a time. This idea is, in itself, interesting because no modification of the original architecture had to be carried out. The latest 10-channel model (U-NetCellDivision10), which includes more channels for better performance, required minimal modification to the original U-Net architecture but also simultaneous imaging of cadherin in addition to histone markers, which may not be a generic solution.

We believe we have provided a general approach for practical use by biologists that can be applied to a range of experimental data, whether that is based on varying numbers of fluorescent channels and/or timepoints. We envisioned that experimental biologists are likely to have several different parameters permissible for measurement based on their specific experimental conditions e.g., different fluorescently labelled proteins (e.g. tubulin) and/or time frames. To accommodate this, we have made it easy and clear in the code on GitHub how these changes can be made. While the model may need some alterations and retraining, the method itself is a generic solution as the same principles apply to very widely used fluorescent imaging techniques.

Since CNN-based methods accept only fixed-size vectors (fixed image size and fixed channel number) as input (and output), the length or time resolution of the extracted sequences should not vary from one experience to another. As such, the method proposed here may lack generalization capabilities, as it would have to be retrained for each experiment with a slightly different temporal resolution. The paper should have compared results with slightly different temporal resolutions to assess its inference robustness toward fluctuations in division speed.

If multiple temporal resolutions are required for a set of experiments, we envision that the model could be trained over a range of these different temporal resolutions. Of course, the temporal resolution, which requires the largest vector would be chosen as the model's fixed number of input channels. Given the depth of the models used and the potential to easily increase this by replacing resnet34 with resnet50 or resnet101 the model would likely be able to cope with this, although we have not specifically tested this. (page 27)

Another approach (not discussed) consists in directly convolving several temporal frames using a 3D CNN (2D+time) instead of a 2D, in order to detect a temporal event. Such an idea shares some similarities with the proposed approach, although in this previous work (Ji et al. TPAMI 2012 and for split detection Nie et al. CCVPR 2016) convolution is performed spatio-temporally, which may present advantages. How does the authors' method compare to such an (also very simple) approach?

We thank the Reviewer for this insightful comment. The text now discusses this (on Pages 8 and 17). Key differences between the models include our incorporation of multiple light channels and the use of much deeper models. We suggest that our method allows for an easy and natural extension to use deeper models for even more demanding tasks e.g. distinguishing between healthy and defective divisions. We also tested our method with ‘difficult conditions’ such as when a wound is present; despite the challenges imposed by the wound (including the discussed reduction in fluorescent intensities near the wound edge), we achieved higher accuracy compared to Nie et al. (accuracy of 78.5% compared to our F1 score of 0.964) using a low-density in vitro system.

Major point 2: innovatory nature of the proposed method.

The authors' idea of exploiting existing channels in the input vector to feed successive frames is interesting, but the natural choice in deep learning for manipulating time series is to use recurrent networks or their newer and more stable variants (LSTM, GRU, attention networks, or transformers). Several papers exploiting such approaches have been proposed for the mitotic division detection task, but they are not mentioned or discussed in this manuscript: Phan et al. 2018, Mao et al. 2019, Kitrungrotaskul et al. 2019, She et al 2020.

An obvious advantage of an LSTM architecture combined with CNN is that it is able to address variable length inputs, therefore time sequences of different lengths, whereas a CNN alone can only be fed with an input of fixed size.

LSTM architectures may produce similar accuracy to the models we employ in our study, however due to the high degree of accuracy we already achieve with our methods, it is hard to see how they would improve the understanding of the biology of wound healing that we have uncovered. Hence, they may provide an alternative way to achieve similar results from analyses of our data. It would also be interesting to see how LTSM architectures would cope with the noisy and difficult wounded data that we have analysed. We agree with the referee that these alternate models could allow an easier inclusion of difference temporal differences in division time (see discussion on Page 20). Nevertheless, we imagine that after selecting a sufficiently large input time/ fluorescent channel input, biologists could likely train our model to cope with a range of division lengths.

Another advantage of some of these approaches is that they rely on unsupervised learning, which can avoid the tedious relabeling of data (Phan et al. 2018, Gilad et al. 2019).

While these are very interesting ideas, we believe these unsupervised methods would struggle under the challenging conditions within ours and others experimental imaging data. The epithelial tissue examined in the present study possesses a particularly high density of cells with overlapping nuclei compared to the other experimental systems these unsupervised methods have been tested on. Another potential problem with these unsupervised methods is the difficulty in distinguishing dynamic debris and immune cells from mitotic cells. Once again despite our experimental data being more complex and difficult, our methods perform better than other methods designed for simpler systems as in Phan et al. 2018 and Gilad et al. 2019; for example, analysis performed on lower density in vitro and unwounded tissues gave best F1 scores for a single video was 0.768 and 0.829 for unsupervised and supervised respectively (Phan et al. 2018). We envision that having an F1 score above 0.9 (and preferably above 0.95), would be crucial for practical use by biologists, hence we believe supervision is currently still required. We expect that retraining our models for use in other experimental contexts will require smaller hand labelled datasets, as they will be able to take advantage of transfer learning (see discussion on Page 4).

References :

We have included these additional references in the revised version of our Manuscript.

Ji, S., Xu, W., Yang, M., & Yu, K. (2012). 3D convolutional neural networks for human action recognition. IEEE transactions on pattern analysis and machine intelligence, 35(1), 221-231. >6000 citations

Nie, W. Z., Li, W. H., Liu, A. A., Hao, T., & Su, Y. T. (2016). 3D convolutional networks-based mitotic event detection in time-lapse phase contrast microscopy image sequences of stem cell populations. In Proceedings of the IEEE Conference on Computer Vision and Pattern Recognition Workshops (pp. 55-62).

Phan, H. T. H., Kumar, A., Feng, D., Fulham, M., & Kim, J. (2018). Unsupervised two-path neural network for cell event detection and classification using spatiotemporal patterns. IEEE Transactions on Medical Imaging, 38(6), 1477-1487.

Gilad, T., Reyes, J., Chen, J. Y., Lahav, G., & Riklin Raviv, T. (2019). Fully unsupervised symmetry-based mitosis detection in time-lapse cell microscopy. Bioinformatics, 35(15), 2644-2653.

Mao, Y., Han, L., & Yin, Z. (2019). Cell mitosis event analysis in phase contrast microscopy images using deep learning. Medical image analysis, 57, 32-43.

Kitrungrotsakul, T., Han, X. H., Iwamoto, Y., Takemoto, S., Yokota, H., Ipponjima, S., ... & Chen, Y. W. (2019). A cascade of 2.5 D CNN and bidirectional CLSTM network for mitotic cell detection in 4D microscopy image. IEEE/ACM transactions on computational biology and bioinformatics, 18(2), 396-404.

Shi, J., Xin, Y., Xu, B., Lu, M., & Cong, J. (2020, November). A Deep Framework for Cell Mitosis Detection in Microscopy Images. In 2020 16th International Conference on Computational Intelligence and Security (CIS) (pp. 100-103). IEEE.

Wolny, A., Cerrone, L., Vijayan, A., Tofanelli, R., Barro, A. V., Louveaux, M., ... & Kreshuk, A. (2020). Accurate and versatile 3D segmentation of plant tissues at cellular resolution. Elife, 9, e57613.

Author Response

Reviewer #1 (Public Review):

Castelán-Sánchez et al. analyzed SARS-CoV-2 genomes from Mexico collected between February 2020 and November 2021. This period spans three major spikes in daily COVID-19 cases in Mexico and the rise of three distinct variants of concern (VOCs; B.1.1.7, P.1., and B.1.617.2). The authors perform careful phylogenetic analyses of these three VOCs, as well as two other lineages that rose to substantial frequency in Mexico, focusing on identifying periods of cryptic transmission (before the lineage was first detected) and introductions to and from the neighboring United States. The figures are well presented and described, and the results add to our understanding of SARS-CoV-2 in Mexico. However, I have some concerns and questions about sampling that could affect the results and conclusions. The authors do not provide any details on the distribution of samples across the various Mexican States, making it hard to evaluate several key conclusions. Although this information is provided in Supplementary Data 2, it is not presented in a way that enables the reader to evaluate if lineages were truly predominant in certain regions of the country, or if these results are attributable purely to sampling bias. Specifically, each lineage is said to be dominant in a particular state or region, but it was not clear to me if sampling across states was even at all-time points. For example, the authors state that most B.1.1.7 genome sampling is from the state of Chihuahua, but it is not clear if this was due to more sequenced samples from that region during the time that B.1.1.7 was circulating, or if the effects of B.1.1.7 were truly differential across the country. The authors do mention sequencing biases several times, but need to be more specific about the nature of this bias and how it could affect their conclusions. It is surprising to see in this manuscript that the B.1.1.7 lineage did not rise above 25% prevalence in the data presented, despite its rapid rise in prevalence in many other parts of the world. This calls into question if the presented frequencies of each lineage are truly representative of what was circulating in Mexico at the time, especially since the coordinated sampling and surveillance program across Mexico did not start until May 2021.

We thank the reviewer for the constructive comments. We recognize the need to better explain how the sequencing efforts in the country were set up and carried out, and this has now been clarified throughout the main text (L43-51, L95-105). A new figure comparing the overall cumulative proportion of genomes generated per state between 2020-2021 is now available as Supplementary Figure 1 c. The cumulative proportion of genomes sampled across states per lineage of interest, and corresponding to the period of circulation of the given lineage, were originally provided as maps in Figures 2-4. This has been further clarified in the Results section and in the corresponding figure legends. We also now provide additional maps representing the geographic distribution of the clades identified per lineage, integrating in the figures the information previously available in Supplementary Data 2, Supplementary Figures 4 and 5. As a note, for our analyses, we used the total cumulative genome data available from the country (and not only that generated by CoViGen-Mex, representing one third of the SARS-CoV-2 genomes from Mexico). This is expected to improve any sampling biases related to the scheme adopted by CoViGenMex, and is now clearly stated in the main text.

However, we believe that there has been a misunderstanding related to the genome sampling scheme adopted by CoViGen-Mex, as ‘coordinated sampling and surveillance program across Mexico did not start until May 2021’. Although it is true that further improvements were implemented after this date (enabling genome sampling and sequencing to become more homogenous across the country), the overall virus genome sequencing in Mexico was already sufficient from February 2021. This is represented by the cumulative number of viral genomes sequenced throughout 2020-2021 (both by CoViGen-Mex and other contributing institutions) correlating to the number of cases officially reported in the country during this time (see Supplementary Figure 1 a). This has now been clarified in the Results section (L94-105). Therefore, we hold that “SARS-CoV-2 sequencing in Mexico has been sufficient to explore the spatial and temporal frequency of viral lineages across national territory, and now to further investigate the number of lineage-specific introduction events, and to characterize the extension and geographic distribution of associated transmission chains, as we present in this study” (L102-105). In this context, “a more homogenous sampling across the country is unlikely to impact our main findings, but could i) help pinpoint additional clades we are currently unable to detect, ii) provide further details on the geographic distribution of clades across other regions of the country, and iii) deliver a higher resolution for the viral spread reconstructions we present” (discussed in L466-470).

For the B.1.1.7 lineage in Mexico, we have clarified the issue raised as follows: “during its circulation period, most B.1.1.7 genomes from Mexico were generated from the state of Chihuahua, with these representing the earliest B.1.1.7-assigned genomes from the country. However, our phylodynamic analysis revealed that only a small proportion of these grouped within a larger clade denoting an extended transmission chain (C2a), with the rest falling within minor clusters, or representing singleton events. Relative to other states, Chihuahua generated an overall lower proportion of viral genomes throughout 2020-2021. Thus, more viral genomes sequenced from a particular state does not necessarily translate into more well-supported clades denoting extended transmission chains, whilst the geographic distribution of clades is somewhat independent to the genome sampling across the country.” (L202-211). Again, these observations are supported by a sufficient overall genome sampling from Mexico.

We would further like to make clear that “our results confirm that the B.1.1.7 lineage reached an overall lower sampling frequency of up to 25% (relative to other virus lineages circulating in the country), as was noted prior to this study (for example, see Zárate et al. 2022)” (L189-193). As similar observations were independently made for other Latin American countries such as Brazil, Chile, and Peru (some with better genome representation than others, like Brazil https://www.gisaid.org/), it is possible that “the overall epidemiological dynamics of the B.1.1.7 in Latin America may have substantially differed from what was observed in the USA and UK. Such differences could be partly explained by competition between cocirculating lineages, exemplified in Mexico by the regional co-circulation of B.1.1.7, P.1 and B.1.1.519. Nonetheless, the lack of a representative number of viral genomes for most of these countries prevents exploring such hypothesis at a larger scale, and further highlights the need to strengthen genomic epidemiology-based surveillance across the region” (now discussed in L372-379). We hope the reviewer considers that the issues raised have now been resolved.

Reviewer #2 (Public Review):

The authors use a series of subsampling methods based on phylogenetic placement and geographic setting, informed by human movement data to control for differences in sampling of SARS-CoV-2 genomes across countries. Of note, the authors show that 2 variants likely arose in Mexico and spread via multiple introductions globally, while other variant waves were driven by repeat introductions into Mexico from elsewhere. Finally, they use human mobility data to assess the impact of movement on transmission within Mexico. Overall, the study is well done and provides nice data on an under-studied country. The authors take a thoughtful approach to subsampling and provide a very thorough analysis. Because of the care given to subsampling and the great challenge that proper subsampling represents for the field of phylodynamics, the paper would benefit from a more thorough exploration of how their migration-informed subsampling procedure impacts their results. This would not only help strengthen the findings of the paper, but would likely provide a useful reference for others doing similar studies. Additionally, I would suggest the authors provide a bit more discussion of this subsampling approach and how it may be useful to others in the discussion section of the paper.

We thank the reviewer for the constructive comments, and appreciate the recognition of our sub-sampling scheme as a valuable tool with potential application in other studies. We acknowledge the need for a ‘more thorough exploration and discussion of how a different migration-informed subsampling approach could impact our results’. To address this issue, “we further sought to validate our migration-informed genome subsampling scheme (applied to B.1.617.2+, representing the best sampled lineage in Mexico). For this, an independent dataset was built using a different migration sub-sampling approach, comprising all countries represented by B.1.617.2+ sequences deposited in GISAID (available up to November 30th 2021). In order to compare the number of introduction events, the new dataset was analysed independently under a time-scaled DTA (as described in Methods Section 4).” (L517-524). In the new dataset, <100 genome sequences from the USA were retained for further analysis (Supplementary Figure 2b), compared to approximately 2000 ‘USA’ genome sequences included in the original B.1.617.2+ alignment. Thus, we expected a lower number of inferred introduction events into Mexico, as an undersampling of viral genome sequences from the USA is likely to result in ‘Mexico’ clades not fully segregating (particularly impacting C5d).

Our original results revealed a minimum number of 142 introduction events into Mexico (95% HPD interval = [125-148]), with 6 clades identified as denoting extended transmission chains. The DTA results derived from the new dataset (subsampling all countries) revealed a minimum number of 84 introduction events into Mexico (95% HPD interval = [81-87]), with again 6 major clades identified. Thus, a significantly lower number of introduction events into Mexico were inferred, as was expected. On the other hand, the number of clades identified were consistent between both datasets, supporting for the robustness of our phylogenetic methodological approach. However, in the new dataset, we observe that C5d displayed a reduced diversity (represented by the AY.113 and AY.100 genomes from Mexico, but excluded the B.1.617.2 genome sampled from the USA). This highlights the relevance of our genome sub-sampling using migration data as a proxy.

In further agreement with these observations, publicly available data on global human mobility (https://migration-demography-tools.jrc.ec.europa.eu/data- hub/index.html?state=5d6005b30045242cabd750a2) shows that migration into Mexico is mostly represented by movements from the USA, followed by Indonesia, Guatemala, Belize and Colombia and Belize. However, the volume of movements from the USA into Mexico is much higher (up to 6 orders of magnitude above the volumes recorded into Mexico from any other country).

Given time constraints related to performing additional analyses, we decided to exclude the subsampling scheme for ‘top ten countries’ suggested by the reviewer. However, we consider that the results derived from the comparison between the original and the new dataset (top-5 vs all countries) is sufficient to support for our migration-informed subsampling approach. A full description of the methodology and the result obtained, as well as a short discussion, is now available as Supplementary Text 2, and Supplementary Figure 2b and 2c. We hope the reviewer considers that the issues raised has been addressed.

Author Response

Reviewer #1 (Public Review):

High resolution mechanistic studies would be instrumental in driving the development of Cas7-11 based biotechnology applications. This work is unfortunately overshadowed by a recent Cell publication (PMID: 35643083) describing the same Cas7-11 RNA-protein complex. However, given the tremendous interest in these systems, it is my opinion that this independent study will still be well cited, if presented well. The authors obviously have been trying to establish a unique angle for their story, by probing deeper into the mechanism of crRNA processing and target RNA cleavage. The study is carried out rigorously. The current version of the manuscript appears to have been rushed out. It would benefit from clarification and text polishing.

We thank the reviewer for the positive and helpful comments that have made the manuscript more impactful.

To summarize the revisions, we have resolved the metal-dependence issue, updated the maps in both main and supplementary figures that support the model, re-organized the labels for clarity, and added the comparison between our and Kato et al.’ structures.

In addition, we describe a new result with an isolated C7L.1 fragment that retains the processing and crRNA binding activities.

Reviewer #2 (Public Review):

In this manuscript, Gowswami et al. solved a cryo-EM structure of Desulfonema ishimotonii Cas7-11 (DiCas7-11) bound to a guiding CRISPR RNA (crRNA) and target RNA. Cas7-11 is of interest due to its unusual architecture as a single polypeptide, in contrast to other type III CRISPR-Cas effectors that are composed of several different protein subunits. The authors have obtained a high-quality cryo-EM map at 2.82 angstrom resolution, allowing them to build a structural model for the protein, crRNA and target RNA. The authors used the structure to clearly identify a catalytic histidine residue in the Cas7-11 Cas7.1 domain that is important for crRNA processing activity. The authors also investigated the effects of metal ions and crRNAtarget base pairing on target RNA cleavage. Finally, the authors used their structure to guide engineering of a compact version of Cas7-11 in which an insertion domain that is disordered in the cryo-EM map was removed. This compact Cas7-11 appears to have comparable cleavage activity to the full-length protein.

The cryo-EM map presented in this manuscript is generally of high quality and the manuscript is very well illustrated. However, some of the map interpretation requires clarification (outlined below). This structure will be valuable as there is significant interest in DiCas7-11 for biotechnology. Indeed, the authors have begun to engineer the protein based on observations from the structure. Although characterization of this engineered Cas7-11 is limited in this study and similar engineering was also performed in a recently published paper (PMID 35643083), this proof-of-principle experiment demonstrates the importance of having such structural information.

The biochemistry experiments presented in the study identify an important residue for crRNA processing, and suggest that target RNA cleavage is not fully metal-ion dependent. Most of these conclusions are based on straightforward structure-function experiments. However, some results related to target RNA cleavage are difficult to interpret as presented. Overall, while the cryo-EM data presented in this work is of high quality, both the structural model and the biochemical results require further clarification as outlined below.

We thank the reviewer for the positive and helpful comments that have made the manuscript more impactful.

To summarize the revisions, we have resolved the metal-dependence issue, updated the maps in both main and supplementary figures that support the model, re-organized the labels for clarity, and added the comparison between our and Kato et al.’ structures.

In addition, we describe a new result with an isolated C7L.1 fragment that retains the processing and crRNA binding activities.

1. The DiCas7-11 structure bound to target RNA was also recently reported by Kato et al. (PMID 35643083). The authors have not cited this work or compared the two structures. While the structures are likely quite similar, it is notable that the structure reported in the current paper is for the wild-type protein and the sample was prepared under reactive conditions, resulting in a partially cleaved target. Kato et al. used a catalytically dead version of Cas7-11 in which the target RNA should remain fully intact. Are there differences in the Cas7-11 structure observed in the presence of a partially cleaved target RNA in comparison to the Kato et al. structure? Such a comparison is appropriate given the similarities between the two reports. A figure comparing the two structures could be included in the manuscript.

We have added a paragraph on page 12 that describe the differences in preparation of the two complexes and their structures. We observed minor differences in the overall protein structure (r.m.s.d. 0.918 Å for 8114 atoms) but did observe quite different interactions between the protein and the first 5’-tag nucleotide (U(-15) vs. G(-15)) due to the different constructs in pre-crRNA, which suggests an importance of U(-15) in forming the processing-competent active site. We added Figure 2-figure supplementary 3 that illustrates the similarities and the differences.

2.The cryo-EM density map is of high quality, but some of the structural model is not fully supported by the experimental data (e.g. protein loops from the alphafold model were not removed despite lack of cryo-EM density). Most importantly, there is little density for the target RNA beyond the site 1 cleavage site, suggesting that the RNA was cleaved and the product was released. However, this region of the RNA was included in the structural model. It is unclear what density this region of the target RNA model was based on. Further discussion of the interpretation of the partially cleaved target RNA is necessary. Were 3D classes observed in various states of RNA cleavage and with varied density for the product RNAs?

We should have made it clear in the Method that multiple maps were used in building the structure but only submitted the post-processed map to reviewers. When using the Relion 4.0’s local resolution estimation-generated map, we observed sufficient density for some of the regions the reviewer is referring to. For instance, the site 1 cleavage density does support the model for the two nucleotides beyond site 1 cleavage site (see the revised Figure 1 & Figure 1- figure supplement 3).

However, there are protein loops that remain lack of convincing density. These include 134141 and 1316-1329 that are now removed from the final coordinate.

The “partially cleaved target RNA” phrase is a result of weak density for nucleotides downstream of site 1 (+2 and +3) but clear density flanking site 2. This feature indicates that cleavage likely had taken place at site 1 but not site 2 in most of the particles went into the reconstruction. To further clarify this phrase, we added “The PFS region plus the first base paired nucleotide (+1*) are not observed.” on page 4 and better indicate which nucleotides are or are not built in our model in Figure 1.

1. The authors argue that site 1 cleavage of target RNA is independent of metal ions. This is a potentially interesting result, but it is difficult to determine whether it is supported by the evidence provided in the manuscript. The Methods section only describes a buffer containing 10 mM MgCl2, but does not describe conditions containing EDTA. How much EDTA was added and was MgCl2 omitted from these samples? In addition, it is unclear whether the site 1 product is visible in Figures 2d and 3d. To my eye, the products that are present in the EDTA conditions on these gels migrated slightly slower than the typical site 1 product. This may suggest an alternate cleavage site or chemistry (e.g. cyclic phosphate is maintained following cleavage). Further experimental details and potentially additional experiments are required to fully support the conclusion that site 1 cleavage may be metal independent.

As we pointed out in response to Reviewer 1’s #8 comment, this conclusion may have been a result of using an older batch of DiCas7-11 that contains degraded fragments.

As shown in the attached figure below, “batch Y” was an older prep from our in-house clone and “batch X” is a newer prep from the Addgene purchased clone (gel on right), and they consistently produce metal-independent (batch Y) or metal-dependent (batch X) cleavage (gel on left). It is possible that the degraded fragments in batch Y carry a metal-independent cleavage activity that is absent in the more pure batch X.

We further performed mass spectrometry analysis of two of the degraded fragments from batch Y (indicated by arrows below) and discovered that these are indeed part of DiCas7-11. We, however, cannot rationalize, without more experimental evidence, why these fragments might have generated metal-independent cleavage at site 1. Therefore, we simply updated all our cleavage results from the new and cleaner prep (batch X) (For instance, Figure 3c). As a result, all references to “metal-independence” were removed.

With regard to the nature of cleaved products, we found both sites could be inhibited by specific 2’-deoxy modifications, consistent with the previous observation that Type III systems generate a 2’, 3’-cyclic product in spite of the metal dependence (for instance, see Hale, C. R., Zhao, P., Olson, S., Duff, M. O., Graveley, B. R., Wells, L., ... & Terns, M. P. (2009). RNA-guided RNA cleavage by a CRISPR RNA-Cas protein complex. Cell, 139(5), 945-956.)

We added this rationale based on the new results and believe that these characterizations are now thorough and conclusive

1. The authors performed an experiment investigating the importance of crRNA-target base pairing on cleavage activity (Figure 3e). However, negative controls for the RNA targets in the absence of crRNA and Cas7-11 were not included in this experiment, making it impossible to determine which bands on the gel correspond to substrates and which correspond to products. This result is therefore not interpretable by the reader and does not support the conclusions drawn by the authors.

Our original gel image (below) does contain these controls but we did not include them for the figure due to space considerations (we should have included it as a supplementary figure). We have now completely updated Figure 3e with much better quality and controls. Both the older and the updated experiments show the same results.

Original gel for Figure 3e containing controls.

Author Response

Reviewer #1 (Public Review):

The idea that because the hippocampal code generates responses that match the most needed variable for each task (time or distance) makes it a predictive code is not fully proved with the analyses provided in the manuscript. For example, in the elapsed time task, there are also place cells and in the fixed-distance travel there are also cells that encode other features. This, rather than a predictive code, can be a regular sample of the environment with an overrepresentation of the more salient variable that animals need to get in order to collect rewards.

We concur with the Reviewer’s reservation. Claims about predictive coding were removed and the following possible account explanation for over-representation was suggested instead:

"These results underscore the flexible coding capabilities of the hippocampus, which are shaped by over-representation of salient variables associated with reward conditions. " (page 1 line 23, page 4 line 27)

In addition, the analysis provided in the manuscript are rather simple, and better controls could be provided. Improving the analytical quantification of the results is necessary to support the main claim.

We improved the quantification, as suggested below by specific comments of the reviewer.

What is the relationship of each type of cell with the speed of the animal?

The cells were assigned to the different types according to their responses while running across all speeds. However, we checked how the speed of the animal affects the peak firing rate of the cells, for each type of cell. Results of this analysis are presented in Author response image 1. Bars represent maximum firing rate of all cells of a given type across runs with the specified speed range (𝒎𝒆𝒂𝒏 ± 𝑺𝑬𝑴).

Author response image 1.

We did not find a significant interaction effect of the speed and the cell-type over the max firing rate (2-way Anova p>0.98).

What is the relationship with the n of trial that the animal has run (first 10 trials, last 10 trials..)?

Some of the animals were subjected to only one type of session. Moreover, they were sometimes trained without recording. Therefore, to answer this question we restricted our analysis to recording sessions where the animal switched from fixed-time to fixed-distance or vice versa. We checked the 20 first runs vs. the last 20 runs (data from 10 runs is not powerful enough for analysis) in See the results in Author response table 1.

Author response table 1.

To assess the dynamics of the coding flexibility, we defined the Time-Distance index (TDI), quantifying the balance between the proportion of distance cells and of time cells at a given time. as (NDistanceCells/NTimeCells)/(NDistanceCells+NTimeCells). The is in the range of [0 ,1] if the majority of cells are classified as distance cells, and in the range of [-1, 0] if the majority of cells are classified as time cells. Chi-square testing for differences in proportions did not reveal significant differences (after correction for multiple comparisons).

The shaded boxes in Author response table 1 indicate the sessions which followed a transition between session types

What is the average firing rate of each neuron?

This information was now added to the titles of the panels in Figure 2 and Figure 2-figure supplement 1.

Is there any relationship between intrinsic firing rate and the type of coding that the cell develops in each task?

In Author response image 2 is a comparison of the firing rates of the Time cells vs the Distance cells.

The distributions are similar (p = 0.975 ,and p = 0.675 for peak firing rate and mean firing rate, respectively, Kolmogorov-Smirnov (KS) test).

Author response image 2.

This figure was added to the supplementary figures (figure 3 - figure supplement 3)

What is the relation of the units of each type with LFP features (theta phase, ripple recruitment)?

We had LFP recordings for 15 out of 18 sessions. A large proportion of the cells showed phase precession (see Author response table 2). An example is shown in Author response image 3. We could not find a significant relation between phase precession and the cell type or the trial type.

The table on the left shows the total cells analyzed, and on the right we show the percentage of cells that had a significant linear fit of the theta phase within 80% of the field width, when analyzed per time (topright) or per distance (bottom-right). FDist/Ftime are Fixed-distance and fixed-time trials and Dist/Time are the cell type.

We did not identify ripple events during treadmill runs.

Author response table 2

Author response image 3

Reviewer #3 (Public Review):

Weaknesses:

The original study of Kraus et al. consisted of 3 rats for which all sessions, including both training and recording, were of one type. Another 3 rats had a hybrid mixture of distance and time sessions. This is mentioned very briefly in the main text.

It would appear that the theory of reward might lead to different predictions that could be verified by comparing these animals session to session at a finer grain. For example, are there examples of cells switching or transforming their “predictive” representations when a large number of trials in on session type is followed by a large number of trials of the opposite type?

For another example, the transition from training to recording could give similar opportunities. It seems at least possible that ignoring these issues could cause a loss of power.

We could not compare a particular cell for switching between encodings since the different types of trial were performed on different days. As an alternative, we compared the populations of cells within the first 20 vs. last 20 trials in recording sessions where the animal switched from fixed-time to fixed-distance or vice versa (see table below). The “Time-Distance balance index” (TDI) is defined as (#DistanceCells#TimeCells)/(#DistanceCells+#TimeCells) and is ranges between 0 and 1 if the majority of cells are classified as distance cells while between -1 to 0 if the majority of cells are classified as time cells.

In all three animals there seems to be a change between the first 20 runs and last 20 runs of the same session, following a switch between trial types. However, this change is significant and with the expected trend only in one of the animals (BK49, p=0.02, chi-square test).

The grayed boxes in Author response table 1 indicate the sessions which followed a transition between session types

Some circularities in the construction and interpretation of the time-cell and distance-cell classifiers are not clearly addressed. The classifiers currently appear to be fit to predict the type of session a cell’s response patterns are observed within. But it is tautological to use the session type to define the cell type. I sense this is ultimately reasonable because of how the classifier is built, but this concern is not addressed or explained.

We regret that the term ‘classifiers’ was not sufficiently precise. We used this term to describe the metrics designed to express the relation between the firing-time and the velocity, in order to classify cells, rather than classifiers that are fit to predict the type of session. We believe this to be the source of the apparent circularity. To circumvent this confusion, we now replaced all places where the term “classifier” was mentioned, with the term “metric”

Author Response

Reviewer #1 (Public Review):

In this manuscript, May et al use H2B overexpression driven by Keratin14 Cre-mediated excision of a loxPstop cassette to quantify bulk chromatin dynamics in the live epidermis. They observe heterogeneity of H2B distribution within the basal stem cell layer and a change in distribution when the stem cells delaminate into the suprabasal layers. They further show that these chromatin rearrangements precede cell fate commitment, as detected by adding another Cre-mediated transgene on top (tetO-Cre mediated Keratin10 reporter). Finally, they generate an MST stem-loop transgene for the keratin 10 transcript and observe transcriptional bursting.

We would like to clarify for the reviewer that the H2B system used is a transgenic allele of histone-2B-GFP that is driven directly by the Keratin-14 promoter (Kanda et al., 1998; Tumbar et al., 2004). This system does not rely on any Cre-mediated excision of the LoxP-stop cassette, and these mice do not carry Cre alleles. We will touch on this point below when addressing the comment on Cre expression in cells and the raised question on whether it influences the quantifications of chromatin compaction.

The manuscript uses elegant in vivo imaging approaches to describe a set of observations that are logically based on a panel of studies that have used genetic approaches to dissect the role of heterochromatin and histone/DNA modifications in epidermal state transitions. In addition, the MST stem-loop analysis is a nice technical advance, confirming transcriptional bursting as a general phenomenon of how transcription is regulated in cells (see work from Daniel Larsson, Jonathan Chubb, Arjun Raj, and others).

We thank the reviewer for their recognition of our contribution to the transcription field. To deepen the connection between our data and previous characterizations of transcriptional dynamics in other systems, we have added new analyses of K10MS2 transcriptional bursting on a finer temporal scale (Fig 5G-K). We find pervasive “transcriptional bursting,” consistent with findings in vitro and in other model organisms, and a surprising variation of burst durations. We believe these additional analyses significantly strengthen our conclusions and the relevance of our study to the overall transcription field.

The value of the study in my view is recapitulating these known phenomena in a live tissue setting with high-quality imaging and careful quantification. Overall, the analyses appear thorough, although the overall changes appear relatively minor, which is perhaps to be expected from imaging bulk H2B distribution as a proxy for chromatin states.

There is one major technical concern that might impact the interpretation of the data. The authors combine Cre lines for their key conclusions (Krt10 reporter and SRF KO) and analyze single cells that thus express very high levels of Cre. Knowing that Cre will target non-loxP sites and is genotoxic, it is possible that the effect of chromatin is due to high levels of Cre expression in single cells rather than specific effects due to cell state transitions. I would encourage the authors to carefully quantify the dose-dependent effects of the Cre protein (independent of the LoxP sites) on chromatin organization. Along these lines, is the phenotype of the SRF KO similar in the presence of two Cre alleles versus just one?

Thank you for these kind words. This is an important potential caveat to consider. We believe that Cre activity does not significantly affect the chromatin compaction profiles for several reasons. First, we interrogated Cre activity. The quantifications in Figure 1A-E and Figure 2B-C are from mice containing K14H2B-GFP allele alone and do not carry any Cre allele. When these data were compared to those from mice that had been treated with a high dose of tamoxifen to induce Cre-mediated recombination in the vast majority of cells, the chromatin compaction profiles were not significantly different (Supp Fig 3C). We have added this comparison to Supplemental Figure 3 and addressed this point in the text (page 9). To further determine whether Cremediated recombination affects our measurement of chromatin compaction, we also analyzed adjacent basal cells with and without Cre activity in the same animal. K14H2BGFP; K14CreER; tdTomato mice were induced with a low dose of tamoxifen such that roughly 65% of epidermal cells underwent Cre recombination as demonstrated by expression of the tdTomato fluorescent reporter (Gallini et al., 2022). They also received a punch biopsy performed on the unimaged ear. Three days post injury and six days after Cre induction, the chromatin compaction profiles of cells positive and negative for Cre-mediated recombination were also not significantly different (Rebuttal Figure 1). Together, these direct comparisons between cells exposed to Cre activity and cells not exposed to Cre activity indicate that Cre activity at levels comparable to those used in our experiments has no measurable effect on our measurements of chromatin compaction.

Rebuttal Figure 1: Effect of Cre expression on chromatin compaction profiles

The second issue is the conclusion of "chromatin spinning". Concluding that chromatin is spinning would in my view require that the authors demonstrate that the nuclear envelope is not moving or is moving less than the chromatin. To support this conclusion the authors should do double imaging for example with LINC complex proteins, an ER/outer nuclear membrane marker, or equivalent.

This is an excellent point. While we expect that the entire nucleus is spinning based on observations others have made in in vitro fibroblasts systems, we describe our observation as “chromatin spinning” instead of “nuclear spinning” because the K14H2B-GFP allele only allows us to directly visualize chromatin itself (Kumar et al., 2014; Zhu et al., 2018).

Unfortunately, LINC complex proteins and nuclear membrane proteins have not been fluorescently tagged in mice, which prevents us from visualizing their dynamics in vivo. To establish these new tools and perform experiments would take more than a year, making it therefore beyond the scope of this current paper. Additionally, their relatively uniform distribution across the nuclear membrane would not allow us to visualize potential spinning of these components. We have made efforts towards the reviewer’s question by asking whether other compartments within the cell also spin in delaminating cells. To do this, we leveraged a mouse line developed by Claudio Franco’s lab (Barbacena et al., 2019), which fluorescently labels both the chromatin (H2B-GFP) and the Golgi (GTS-mCherry). As expected, this model showed a perinuclear and polarized Golgi in skin fibroblasts (Rebuttal Figure 2). However, this tool is incompatible with our questions in epidermal cells for a few reasons. First, the system is toxic to epithelial cells in vivo, resulting in apoptosis, nuclear fragmentation, and binucleate cells. Second, the Golgi is not discretely polarized (or even perinuclear) in epithelial cells (Rebuttal Figure 2). As such, although we observe chromatin spinning in delaminating basal cells, we are uncertain as to whether the whole nucleus or any other cellular compartments are spinning in these cells.

Rebuttal Figure 2: Interrogation of intracellular spinning

Given the above reasoning and efforts, we have altered the text and specified that we only have the capacity to visualize chromatin through the H2B-GFP allele and that we hypothesize the entire nucleus is spinning (page 11).

Reviewer #2 (Public Review):

In this work entitled "Live imaging reveals chromatin compaction transitions and dynamic transcriptional bursting during stem cell differentiation in vivo" the authors use a combination of genetic and imaging tools to characterize dynamic changes in chromatin compaction of cells undergoing epidermal stem cell differentiation and to relate chromatin compaction to transcriptional regulation in vivo. They track this phenomenon by imaging the epithelium at the ear of live mice, thus in a physiological context. By following individual nuclei expressing H2B-GFP along time ranges of hours and up to 3 days, they develop a strategy to quantify the profile of chromatin compaction across different epidermal layers based on normalized intensity profiles of H2B-GFP. They observe that cells belonging to the basal stem cell layer display a considerable level of internuclear variability in chromatin compaction that is cell-cycle independent. Instead, intercellular variability in chromatin compaction appears more related to the differentiation status of the cells as it is stable in the hours range but dynamic in the days range. The authors show that differentiated nuclei in the spinous layer exhibit higher chromatin compaction. They also identified a subset of cells in the basal stem layer with an intermediate profile of chromatin compaction and with the dynamic expression of the early differentiation marker keratin 10. Lastly, they show that the expression of keratin-10 precedes the chromatin compaction establishing relevant temporal relationships in the process of epidermal differentiation.

This work includes a number of challenging approaches and techniques since it is carried out in living mice. Also, it provides nice tools and methods to study chromatin structure in vivo during multiple days and within a differentiation physiological system. On the other hand, the results are descriptive and, in some respect, expected in line with previous observations.

Thank you very much for this great summary, kind words, and the recommendations listed below. We will address each of them specifically. We have also deepened the analysis of transcriptional dynamics in ways that are more comparable with how other groups have studied transcription and included those results in Figure 5.

References

Kanda, T., Sullivan, K.F., and Wahl, G.M. (1998). Histone–GFP fusion protein enables sensitive analysis of chromosome dynamics in living mammalian cells. Current Biology 8, 377–385. 10.1016/S09609822(98)70156-3.

Tumbar, T., Guasch, G., Greco, V., Blanpain, C., Lowry, W.E., Rendl, M., and Fuchs, E. (2004). Defining the epithelial stem cell niche in skin. Science 303, 359–363. 10.1126/science.1092436.

Kumar, A., Maitra, A., Sumit, M., Ramaswamy, S., and Shivashankar, G.V. (2014). Actomyosin contractility rotates the cell nucleus. Sci Rep 4, 3781. 10.1038/srep03781.

Zhu, R., Liu, C., and Gundersen, G.G. (2018). Nuclear positioning in migrating fibroblasts. Seminars in Cell & Developmental Biology 82, 41–50. 10.1016/j.semcdb.2017.11.006.

Sara Gallini, Nur-Taz Rahman, Karl Annusver, David G. Gonzalez, Sangwon Yun, Catherine Matte-Martone, Tianchi Xin, Elizabeth Lathrop, Kathleen C. Suozzi, Maria Kasper, Valentina Greco . Injury suppresses Ras cell competitive advantage through enhanced wild-type cell proliferation.<br /> bioRxiv 2022.01.05.475078; doi: https://doi.org/10.1101/2022.01.05.475078

Pedro Barbacena, Marie Ouarné, Jody J Haigh, Francisca F Vasconcelos, Anna Pezzarossa, Claudio A Franco. GNrep mouse: A reporter mouse for front-rear cell polarity. Genesis 2019 Jun. DOI: 10.1002/dvg.23299

Cristiana M Pineda, Sangbum Park, Kailin R Mesa, Markus Wolfel, David G Gonzalez, Ann M Haberman, Panteleimon Rompolas, Valentina Greco. Intravital imaging of hair follicle regeneration in the mouse. Nature Protocols 2015 July. DOI: 10.1038/nprot.2015.070

Author Response

Reviewer #1 (Public Review):

The work by Yijun Zhang and Zhimin He at al. analyzes the role of HDAC3 within DC subsets. Using an inducible ERT2-cre mouse model they observe the dependency of pDCs but not cDCs on HDAC3. The requirement of this histone modifier appears to be early during development around the CLP stage. Tamoxifen treated mice lack almost all pDCs besides lymphoid progenitors. Through bulk RNA seq experiment the authors identify multiple DC specific target gens within the remaining pDCs and further using Cut and Tag technology they validate some of the identified targets of HDAC3. Collectively the study is well executed and shows the requirement of HDAC3 on pDCs but not cDCs, in line with the recent findings of a lymphoid origin of pDC.

1) While the authors provide extensive data on the requirement of HDAC3 within progenitors, the high expression of HDAC3 in mature pDCs may underly a functional requirement. Have you tested INF production in CD11c cre pDCs? Are there transcriptional differences between pDCs from HDAC CD11c cre and WT mice?

We greatly appreciate the reviewer’s point. We have confirmed that Hdac3 can be efficiently deleted in pDCs of Hdac3fl/fl-CD11c Cre mice (Figure 5-figure supplement 1 in revised manuscript). Furthermore, in those Hdac3fl/fl-CD11c Cre mice, we have observed significantly decreased expression of key cytokines (Ifna, Ifnb, and Ifnl) by pDCs upon activation by CpG ODN (shown in Author response image 1). Therefore, HDAC3 is also required for proper pDC function. However, we have yet to conduct RNA-seq analysis comparing pDCs from HDAC CD11c cre and WT mice.

Author response image 1.

Cytokine expression in Hdac3 deficient pDCs upon activation

2) A more detailed characterization of the progenitor compartment that is compromised following depletion would be important, as also suggested in the specific points.

We thank the reviewer for this constructive suggestion. We have performed thorough analysis of the phenotype of hematopoietic stem cells and progenitor cells at various developmental stages in the bone marrow of Hdac3 deficient mice, based on the gating strategy from the recommended reference. Briefly, we analyzed the subpopulations of progenitors based on the description in the published report by "Pietras et al. 2015", namely MPP2, MPP3 and MPP4, using the same gating strategy for hematopoietic stem/progenitor cells. As shown in Author response image 2 and Author response image 3, we found that the number of LSK cells was increased in Hdac3 deficient mice, especially the subpopulations of MPP2 and MPP3, whereas no significant changes in MPP4. In contrast, the numbers of LT-HSC, ST-HSC and CLP were all dramatically decreased. This result has been optimized and added as Figure 3A in revised manuscript. The relevant description has been added and underlined in the revised manuscript Page 6 Line 164-168.

Author response image 2.

Gating strategy for hematopoietic stem/progenitor cells in bone marrow.

Author response image 3.

Hematopoietic stem/progenitor cells in Hdac3 deficient mice

Reviewer #2 (Public Review):

In this article Zhang et al. report that the Histone Deacetylase-3 (HDAC3) is highly expressed in mouse pDC and that pDC development is severely affected both in vivo and in vitro when using mice harbouring conditional deletion of HDAC3. However, pDC numbers are not affected in Hdac3fl/fl Itgax-Cre mice, indicating that HDCA3 is dispensable in CD11c+ late stages of pDC differentiation. Indeed, the authors provide wide experimental evidence for a role of HDAC3 in early precursors of pDC development, by combining adoptive transfer, gene expression profiling and in vitro differentiation experiments. Mechanistically, the authors have demonstrated that HDAC3 activity represses the expression of several transcription factors promoting cDC1 development, thus allowing the expression of genes involved in pDC development. In conclusion, these findings reveals HDAC3 as a key epigenetic regulator of the expression of the transcription factors required for pDC vs cDC1 developmental fate.

These results are novel and very promising. However, supplementary information and eventual further investigations are required to improve the clarity and the robustness of this article.

Major points

1) The gating strategy adopted to identify pDC in the BM and in the spleen should be entirely described and shown, at least as a Supplementary Figure. For the BM the authors indicate in the M & M section that they negatively selected cells for CD8a and B220, but both markers are actually expressed by differentiated pDC. However, in the Figures 1 and 2 pDC has been shown to be gated on CD19- CD11b- CD11c+. What is the precise protocol followed for pDC gating in the different organs and experiments?

We apologize for not clearly describing the protocols used in this study. Please see the detailed gating strategy for pDC in bone marrow, and for pDC and cDC in spleen (Figure 4 and Figure 5). These information are now added to Figure1−figure supplement 3, The relevant description has been underlined in Page 5 Line 113-116, in revised manuscript.

We would like to clarify that in our study, we used two different panels of antibody cocktails, one for bone marrow Lin- cells, including mAbs to CD2/CD3/TER-119/Ly6G/B220/CD11b/CD8/CD19; the other for DC enrichment, including mAbs to CD3/CD90/TER-119/Ly6G/CD19. We included B220 in the Lineage cocktails to deplete B cells and pDCs, in order to enrich for the progenitor cells from bone marrow. However, when enriching for the pDC and cDC, B220 or CD8a were not included in the cocktail to avoid depletion of pDC and cDC1 subsets . For the flow cytometry analysis of pDCs, we gated pDCs as the CD19−CD11b−CD11c+B220+SiglecH+ population in both bone marrow and spleen. The relevant description has been underlined in the revised manuscript Page 16 Line 431-434.

2) pDC identified in the BM as SiglecH+ B220+ can actually contain DC precursors, that can express these markers, too. This could explain why the impact of HDAC3 deletion appears stronger in the spleen than in the BM (Figures 1A and 2A). Along the same line, I think that it would important to show the phenotype of pDC in control vs HDAC3-deleted mice for the different pDC markers used (SiglecH, B220, Bst2) and I would suggest to include also Ly6D, taking also in account the results obtained in Figures 4 and 7. Finally, as HDCA3 deletion induces downregulation of CD8a in cDC1 and pDC express CD8a, it would important to analyse the expression of this marker on control vs HDAC3-deleted pDC.

We agree with the reviewer’s points. In the revised manuscript, we incorporated major surface markers, including Siglec H, B220, Ly6D, and PDCA-1, all of which consistently demonstrated a substantial decrease in the pDC population in Hdac3 deficient mice. Moreover, we did notice that Ly6D+ pDCs showed higher degree of decrease in Hdac3 deficient mice. Additionally, percentage and number of both CD8+ pDC and CD8- pDC were decreased in Hdac3 deficient mice (Author response image 4). These results are shown in Figure1−figure supplement 4 of the revised manuscript. The relevant description has been added and underlined in the revised manuscript Page 5 Line 121-125.

Author response image 4.

Bone marrow pDCs in Hdac3 deficient mice revealed by multiple surface markers

3) How do the authors explain that in the absence of HDAC3 cDC2 development increased in vivo in chimeric mice, but reduced in vitro (Figures 2B and 2E)?

As shown in the response to the Minor point 5 of Reviewer#1. Briefly, we suggested that the variabilities maybe explained by the timing of anaysis after HDAC3 deletion. In Figure 2C, we analyzed cells from the recipients one week after the final tamoxifen treatment and observed no significant change in the percentage of cDC2 when further pooled all the experiment data. In Figure 2E, where tamoxifen was administered at Day 0 in Flt3L-mediated DC differentiation in vitro, the DC subsets generated were then analyzed at different time points. We observed no significant changes in cDCs and cDC2 at Day 5, but decreases in the percentage of cDC2 were observed at Day 7 and Day 9. This suggested that the cDC subsets at Day 5 might have originated from progenitors at a later stage, while those at Day 7 and Day 9 might originate form the earlier progenitors. Therefore, based on these in vitro and in vivo experiments, we believe that the variation in the cDC2 phenotype might be attributed to the progenitors at different stages that generated these cDCs.

4) More generally, as reported also by authors (line 207), the reconstitution with HDAC3-deleted cells is poorly efficient. Although cDC seem not to be impacted, are other lymphoid or myeloid cells affected? This should be expected as HDAC3 regulates T and B development, as well as macrophage function. This should be important to know, although this does not call into question the results shown, as obtained in a competitive context.

In this study, we found no significant influence on T cells, mature B cells or NK cells, but immature B cells were significantly decreased, in Hdac3-ERT2-Cre mice after tamoxifen treatment (Figure 6). However, in the bone marrow chimera experiments, the numbers of major lymphoid cells were decreased due to the impaired reconstitution capacity of Hdac3 deficient progenitors. Consistent with our finding, it has been reported that HDAC3 was required for T cell and B cell generation, in HDAC3-VavCre mice (Summers et al., 2013), and was necessary for T cell maturation (Hsu et al., 2015). Moreover, HDAC3 is also required for the expression of inflammatory genes in macrophages upon activation (Chen et al., 2012; Nguyen et al., 2020).

5) What are the precise gating strategies used to identify the different hematopoietic precursors in the Figure 4 ? In particular, is there any lineage exclusion performed?

We apologize for not describing the experimental procedures clearly. In this study we enriched the lineage negative (Lin−) cells from the bone marrow using a Lineage-depleting antibody cocktail including mAbs to CD2/CD3/TER-119/Ly6G/B220/CD11b/CD8/CD19. We also provide the gating strategy implemented for sorting LSK and CDP populations from the Lin− cells in the bone marrow (Author response image 5), shown in the Figure 3A and Figure4−figure supplement 1 of revised manuscript.

Author response image 5.

Gating strategy for LSK, CD115+ CDP and CD115− CDP in bone marrow

6) Moreover, what is the SiglecH+ CD11c- population appearing in the spleen of mice reconstituted with HDAC3-deleted CDP, in Fig 4D?

We also noticed the appearance of a SiglecH+CD11c− cell population in the spleen of recipient mice reconstituted with HDAC3-deficient CD115−CDPs, while the presence of this population was not as significant in the HDAC3-Ctrl group, as shown in Figure 4D. We speculate that this SiglecH+CD11c− cell population might represent some cells at a differentiation stage earlier than pre-DCs. Alternatively, the relatively increased percentage of this population derived from HDAC3-deficient CD115−CDP might be due to the substantially decreased total numbers of DCs. This could be clarified by further analysis using additional cell surface markers.

7) Finally, in Fig 4H, how do the authors explain that Hdac3fl/fl express Il7r, while they are supposed to be sorted CD127- cells?

This is indeed an interesting question. In this study, we confirmed that CD115−CDPs were isolated from the surface CD127− cell population for RNA-seq analysis, and the purity of the sorted cells were checked (Author response image 6), as shown in Figure4−figure supplement 1 in revised manuscript.

The possible explanation for the expression of Il7r mRNA in some HDAC3fl/fl CD115−CDPs, as revealed in Figure 4H by RNA-seq analysis, could be due to a very low level of cell surface expression of CD127, these cells therefore could not be efficiently excluded by sorting for surface CD127- cells.

Author response image 6.

CD115−CDPs sorting from Hdac3-Ctrl and Hdac3-KO mice

8) What is known about the expression of HDAC3 in the different hematopoietic precursors analysed in this study? This information is available only for a few of them in Supplementary Figure 1. If not yet studied, they should be addressed.

We conducted additional analysis to address the expression of Hdac3 in various hematopoietic progenitor cells at different stages, based on the RNA-seq analyis. The data revealed a relatively consistent level of Hdac3 expression in progenitor populations, including HSC, MMP4, CLP, CDP and BM pDCs (Author response image 7). That suggests that HDAC3 may play an important role in the regulation of hematopoiesis at multiple stages. This information is now added in Figure1−figure supplement 1B of revised manuscript.

Author response image 7.

Hdac3 expression in hematopoietic progenitor cells

9) It would be highly informative to extend CUT and Tag studies to Irf8 and Tcf4, if this is technically feasible.

We totally agree with the reviewer. We have indeed attempted using CUT and Tag study to compare the binding sites of IRF8 and TCF4 in wild-type and Hdac3-deficient pDCs. However, it proved that this is technically unfeasible to get reliable results due to the limited number of cells we could obtain from the HDAC3 deficient mice. We are committed to explore alternative approaches or technologies in future studies to address this issue.

Author response:

Reviewer #1 (Public Review):

How does the brain respond to the input of different complexity, and does this ability to respond change with age?

The study by Lalwani et al. tried to address this question by pulling together a number of neuroscientific methodologies (fMRI, MRS, drug challenge, perceptual psychophysics). A major strength of the paper is that it is backed up by robust sample sizes and careful choices in data analysis, translating into a more rigorous understanding of the sensory input as well as the neural metric. The authors apply a novel analysis method developed in human resting-state MRI data on task-based data in the visual cortex, specifically investigating the variability of neural response to stimuli of different levels of visual complexity. A subset of participants took part in a placebo-controlled drug challenge and functional neuroimaging. This experiment showed that increases in GABA have differential effects on participants with different baseline levels of GABA in the visual cortex, possibly modulating the perceptual performance in those with lower baseline GABA. A caveat is that no single cohort has taken part in all study elements, ie visual discrimination with drug challenge and neuroimaging. Hence the causal relationship is limited to the neural variability measure and does not extend to visual performance. Nevertheless, the consistent use of visual stimuli across approaches permits an exceptionally high level of comparability across (computational, behavioural, and fMRI are drawing from the same set of images) modalities. The conclusions that can be made on such a coherent data set are strong.

The community will benefit from the technical advances, esp. the calculation of BOLD variability, in the study when described appropriately, encouraging further linkage between complementary measures of brain activity, neurochemistry, and signal processing.

Thank you for your review. We agree that a future study with a single cohort would be an excellent follow-up.

Reviewer #2 (Public Review):

Lalwani et al. measured BOLD variability during the viewing of houses and faces in groups of young and old healthy adults and measured ventrovisual cortex GABA+ at rest using MR spectroscopy. The influence of the GABA-A agonist lorazepam on BOLD variability during task performance was also assessed, and baseline GABA+ levels were considered as a mediating variable. The relationship of local GABA to changes in variability in BOLD signal, and how both properties change with age, are important and interesting questions. The authors feature the following results: 1) younger adults exhibit greater task-dependent changes in BOLD variability and higher resting visual cortical GABA+ content than older adults, 2) greater BOLD variability scales with GABA+ levels across the combined age groups, 3) administration of a GABA-A agonist increased condition differences in BOLD variability in individuals with lower baseline GABA+ levels but decreased condition differences in BOLD variability in individuals with higher baseline GABA+ levels, and 4) resting GABA+ levels correlated with a measure of visual sensory ability derived from a set of discrimination tasks that incorporated a variety of stimulus categories.

Strengths of the study design include the pharmacological manipulation for gauging a possible causal relationship between GABA activity and task-related adjustments in BOLD variability. The consideration of baseline GABA+ levels for interpreting this relationship is particularly valuable. The assessment of feature-richness across multiple visual stimulus categories provided support for the use of a single visual sensory factor score to examine individual differences in behavioral performance relative to age, GABA, and BOLD measurements.

Weaknesses of the study include the absence of an interpretation of the physiological mechanisms that contribute to variability in BOLD signal, particularly for the chosen contrast that compared viewing houses with viewing faces.

Whether any of the observed effects can be explained by patterns in mean BOLD signal, independent of variability would be useful to know.

One of the first pre-processing steps of computing SDBOLD involves subtracting the block-mean from the fMRI signal for each task-condition. Therefore, patterns observed in BOLD signal variability are not driven by the mean-BOLD differences. Moreover, as noted above, to further confirm this, we performed additional mean-BOLD based analysis (See Supplementary Materials Pg 3). Results suggest that ∆⃗ MEANBOLD is actually larger in older adults vs. younger adults (∆⃗ SDBOLD exhibited the opposite pattern), but more importantly ∆⃗ MEANBOLD is not correlated with GABA or with visual performance. This is also consistent with prior research (Garrett et.al. 2011, 2013, 2015, 2020) that found MEANBOLD to be relatively insensitive to behavioral performance.

The positive correlation between resting GABA+ levels and the task-condition effect on BOLD variability reaches significance at the total group level, when the young and old groups are combined, but not separately within each group. This correlation may be explained by age-related differences since younger adults had higher values than older adults for both types of measurements. This is not to suggest that the relationship is not meaningful or interesting, but that it may be conceptualized differently than presented.

Thank you for this important point. The relationship between GABA and ∆⃗ SDBOLD shown in Figure 3 is also significant within each age-group separately (Line 386-388). The model used both age-group and GABA as predictors of ∆⃗ SDBOLD and found that both had a significant effect, while the Age-group x GABA interaction was not significant. The effect of age on ∆⃗ SDBOLD therefore does not completely explain the observed relationship between GABA and ∆⃗ SDBOLD because this latter effect is significant in both age-groups individually and in the whole sample even when variance explained by age is accounted for. The revision clarifies this important point (Ln 488-492). Thanks for raising it.

Two separate dosages of lorazepam were used across individuals, but the details of why and how this was done are not provided, and the possible effects of the dose are not considered.

Good point. We utilized two dosages to maximize our chances of finding a dosage that had a robust effect. The specific dosage was randomly assigned across participants and the dosage did not differ across age-groups or baseline GABA levels. We also controlled for the drug-dosage when examining the role of drug-related shift in ∆⃗ SDBOLD. We have clarified these points in the revision and highlighted the analysis that found no effect of dosage on drug-related shift in ∆⃗ SDBOLD (Line 407-418).

The observation of greater BOLD variability during the viewing of houses than faces may be specific to these two behavioral conditions, and lingering questions about whether these effects generalize to other types of visual stimuli, or other non-visual behaviors, in old and young adults, limit the generalizability of the immediate findings.

We agree that examining the factors that influence BOLD variability is an important topic for future research. In particular, although it is increasingly well known that variability modulation itself can occur in a host of different tasks and research contexts across the lifespan (see Garrett et al., 2013 Waschke et al., 2021), to address the question of whether variability modulation occurs directly in response to stimulus complexity in general, it will be important for future work to examine a range of stimulus categories beyond faces and houses. Doing so is indeed an active area of research in Dr. Garrett’s group, where visual stimuli from many different categories are examined (e.g., for a recent approach, see Waschke et.al.,2023 (biorxiv)). Regardless, only face and house stimuli were available in the current dataset. We therefore exploited the finding that BOLD variability tends to be larger for house stimuli than for face stimuli (in line with the HMAX model output) to demonstrate that the degree to which a given individual modulates BOLD variability in response to stimulus category is related to their age, to GABA levels, and to behavioral performance.

The observed age-related differences in patterns of BOLD activity and ventrovisual cortex GABA+ levels along with the investigation of GABA-agonist effects in the context of baseline GABA+ levels are particularly valuable to the field, and merit follow-up. Assessing background neurochemical levels is generally important for understanding individualized drug effects. Therefore, the data are particularly useful in the fields of aging, neuroimaging, and vision research.

Thank you, we agree!

Reviewer #3 (Public Review):

The role of neural variability in various cognitive functions is one of the focal contentions in systems and computational neuroscience. In this study, the authors used a largescale cohort dataset to investigate the relationship between neural variability measured by fMRI and several factors, including stimulus complexity, GABA levels, aging, and visual performance. Such investigations are valuable because neural variability, as an important topic, is by far mostly studied within animal neurophysiology. There is little evidence in humans. Also, the conclusions are built on a large-scale cohort dataset that includes multi-model data. Such a dataset per se is a big advantage. Pharmacological manipulations and MRS acquisitions are rare in this line of research. Overall, I think this study is well-designed, and the manuscript reads well. I listed my comments below and hope my suggestions can further improve the paper.

Strength:

1). The study design is astonishingly rich. The authors used task-based fMRI, MRS technique, population contrast (aging vs. control), and psychophysical testing. I appreciate the motivation and efforts for collecting such a rich dataset.

2) The MRS part is good. I am not an expert in MRS so cannot comment on MRS data acquisition and analyses. But I think linking neural variability to GABA in humans is in general a good idea. There has been a long interest in the cause of neural variability, and inhibition of local neural circuits has been hypothesized as one of the key factors. 3. The pharmacological manipulation is particularly interesting as it provides at least evidence for the causal effects of GABA and deltaSDBOLD. I think this is quite novel.

Weakness:

1) I am concerned about the definition of neural variability. In electrophysiological studies, neural variability can be defined as Poisson-like spike count variability. In the fMRI world, however, there is no consensus on what neural variability is. There are at least three definitions. One is the variability (e.g., std) of the voxel response time series as used here and in the resting fMRI world. The second is to regress out the stimulusevoked activation and only calculate the std of residuals (e.g., background variability). The third is to calculate variability of trial-by-trial variability of beta estimates of general linear modeling. It currently remains unclear the relations between these three types of variability with other factors. It also remains unclear the links between neuronal variability and voxel variability. I don't think the computational principles discovered in neuronal variability also apply to voxel responses. I hope the authors can acknowledge their differences and discuss their differences.

These are very important points, thank you for raising them. Although we agree that the majority of the single cell electrophysiology world indeed seems to prefer Poisson-like spiking variability as an easy and tractable estimate, it is certainly not the only variability approach in that field (e.g., entropy; see our most recent work in humans where spiking entropy outperforms simple spike counts to predict memory performance; Waschke et al., 2023, bioRxiv). In LFP, EEG/MEG and fMRI, there is indeed no singular consensus on what variability “is”, and in our opinion, that is a good thing. We have reported at length in past work about entire families of measures of signal variability, from simple variance, to power, to entropy, and beyond (see Table 1 in Waschke et al, 2021, Neuron). In principle, these measures are quite complementary, obviating the need to establish any single-measure consensus per se. Rather than viewing the three measures of neural variability that the reviewer mentioned as competing definitions, we prefer to view them as different sources of variance. For example, from each of the three sources of variance the reviewer suggests, any number of variability measures could be computed.

The current study focuses on using the standard deviation of concatenated blocked time series separately for face and house viewing conditions (this is the same estimation approach used in our very earliest studies on signal variability; Garrett et al., 2010, JNeurosci). In those early studies, and nearly every one thereafter (see Waschke et al., 2021, Neuron), there is no ostensible link between SDBOLD (as we normaly compute it) and average BOLD from either multivariate or GLM models; as such, we do not find any clear difference in SDBOLD results whether or not average “evoked” responses are removed or not in past work. This is perhaps also why removing ERPs from EEG time series rarely influences estimates of variability in our work (e.g., Kloosterman et al., 2020, eLife).

The third definition the reviewer notes refers to variability of beta estimates over trials. Our most recent work has done exactly this (e.g., Skowron et al., 2023, bioRxiv), calculating the SD even over single time point-wise beta estimates so that we may better control the extraction of time points prior to variability estimation. Although direct comparisons have not yet been published by us, variability over single TR beta estimates and variability over the time series without beta estimation are very highly correlated in our work (in the .80 range; e.g., Kloosterman et al., in prep).

Re: the reviewer’s point that “It also remains unclear the links between neuronal variability and voxel variability. I don’t think the computational principles discovered in neuronal variability also apply to voxel responses. I hope the authors can acknowledge their differences and discuss their differences.” If we understand correctly, the reviewer maybe asking about within-person links between single-cell neuronal variability (to allow Poisson-like spiking variability) and voxel variability in fMRI? No such study has been conducted to date to our knowledge (such data almost don’t exist). Or rather, perhaps the reviewer is noting a more general point regarding the “computational principles” of variability in these different domains? If that is true, then a few points are worth noting. First, there is absolutely no expectation of Poisson distributions in continuous brain imaging-based time series (LFP, E/MEG, fMRI). To our knowledge, such distributions (which have equivalent means and variances, allowing e.g., Fano factors to be estimated) are mathematically possible in spiking because of the binary nature of spikes; when mean rates rise, so too do variances given that activity pushes away from the floor (of no activity). In continuous time signals, there is no effective “zero”, so a mathematical floor does not exist outright. This is likely why means and variances are not well coupled in continuous time signals (see Garrett et al., 2013, NBR; Waschke et al., 2021, Neuron); anything can happen. Regardless, convergence is beginning to be revealed between the effects noted from spiking and continuous time estimates of variability. For example, we show that spiking variability can show a similar, behaviourally relevant coupling to the complexity of visual input (Waschke et al., 2023, bioRxiv) as seen in the current study and in past work (e.g., Garrett et al., 2020, NeuroImage). Whether such convergence reflects common computational principles of variability remains to be seen in future work, despite known associations between single cell recordings and BOLD overall (e.g., Logothetis and colleagues, 2001, 2002, 2004, 2008).

Given the intricacies of these arguments, we don’t currently include this discussion in the revised text. However, we would be happy to include aspects of this content in the main paper if the reviewer sees fit.

2) If I understand it correctly, the positive relationship between stimulus complexity and voxel variability has been found in the author's previous work. Thus, the claims in the abstract in lines 14-15, and section 1 in results are exaggerated. The results simply replicate the findings in the previous work. This should be clearly stated.

Good point. Since this finding was a replication and an extension, we reported these results mostly in the supplementary materials. The stimulus set used for the current study is different than Garrett et.al. 2020 and therefore a replication is important. Moreover, we have extended these findings across young and older adults (previous work was based on older adults alone). We have modified the text to clarify what is a replication and what part are extension/novel about the current study now (Line 14, 345 and 467). Thanks for the suggestion.

3) It is difficult for me to comprehend the U-shaped account of baseline GABA and shift in deltaSDBOLD. If deltaSDBOLD per se is good, as evidenced by the positive relationship between brainscore and visual sensitivity as shown in Fig. 5b and the discussion in lines 432-440, why the brain should decrease deltaSDBOLD ?? or did I miss something? I understand that "average is good, outliers are bad". But a more detailed theory is needed to account for such effects.

When GABA levels are increased beyond optimal levels, neuronal firing rates are reduced, effectively dampening neural activity and limiting dynamic range; in the present study, this resulted in reduced ∆⃗ SDBOLD. Thus, the observed drug-related decrease in ∆⃗ SDBOLD was most present in participants with already high levels of GABA. We have now added an explanation for the expected inverted-U (Line 523-546). The following figure tries to explain this with a hypothetical curve diagram and how different parts of Fig 4 might be linked to different points in such a curve.

Author response image 1.

Line 523-546 – “We found in humans that the drug-related shift in ∆⃗ SDBOLD could be either positive or negative, while being negatively related to baseline GABA. Thus, boosting GABA activity with drug during visual processing in participants with lower baseline GABA levels and low levels of ∆⃗ SDBOLD resulted in an increase in ∆⃗ SDBOLD (i.e., a positive change in ∆⃗ SDBOLD on drug compared to off drug). However, in participants with higher baseline GABA levels and higher ∆⃗ SDBOLD, when GABA was increased presumably beyond optimal levels, participants experienced no-change or even a decrease in∆⃗ SDBOLD on drug. These findings thus provide the first evidence in humans for an inverted-U account of how GABA may link to variability modulation.

Boosting low GABA levels in older adults helps increase ∆⃗ SDBOLD, but why does increasing GABA levels lead to reduced ∆⃗ SDBOLD in others? One explanation is that higher than optimal levels of inhibition in a neuronal system can lead to dampening of the entire network. The reduced neuronal firing decreases the number of states the network can visit and decreases the dynamic range of the network. Indeed, some anesthetics work by increasing GABA activity (for example propofol a general anesthetic modulates activity at GABAA receptors) and GABA is known for its sedative properties. Previous research showed that propofol leads to a steeper power spectral slope (a measure of the “construction” of signal variance) in monkey ECoG recordings (Gao et al., 2017). Networks function optimally only when dynamics are stabilized by sufficient inhibition. Thus, there is an inverted-U relationship between ∆⃗ SDBOLD and GABA that is similar to that observed with other neurotransmitters.”

4) Related to the 3rd question, can you show the relationship between the shift of deltaSDBOLD (i.e., the delta of deltaSDBOLD) and visual performance?

We did not have data on visual performance from the same participants that completed the drug-based part of the study (Subset1 vs 3; see Figure 1); therefore, we unfortunately cannot directly investigate the relationship between the drug-related shift of ∆⃗ SDBOLD and visual performance. We have now highlighted that this as a limitation of the current study (Line 589-592), where we state: One limitation of the current study is that participants who received the drug-manipulation did not complete the visual discrimination task, thus we could not directly assess how the drug-related change in ∆⃗ SDBOLD impacted visual performance.

5) Are the dataset openly available?? I didn't find the data availability statement.

An excel-sheet with all the processed data to reproduce figures and results has been included in source data submitted along with the manuscript along with a data dictionary key for various columns. The raw MRI, MRS and fMRI data used in the current manuscript was collected as a part of a larger (MIND) study and will eventually be made publicly available on completion of the study (around 2027). Before that time, the raw data can be obtained for research purposes upon reasonable request. Processing code will be made available on GitHub.

Author Response

Reviewer #1 (Public Review):

The manuscript by Lujan and colleagues describes a series of cellular phenotypes associated with the depletion of TANGO2, a poorly characterized gene product but relevant to neurological and muscular disorders. The authors report that TANGO2 associates with membrane-bound organelles, mainly mitochondria, impacting in lipid metabolism and the accumulation of reactive-oxygen species. Based on these observations the authors speculate that TANGO2 function in Acyl-CoA metabolism.

The observations are generally convincing and most of the conclusions appear logical. While the function of TANGO2 remains unclear, the finding that it interferes with lipid metabolism is novel and important. This observation was not developed to a great extent and based on the data presented, the link between TANGO2 and acyl-CoA, as proposed by the authors, appears rather speculative.

We thank you for your advice and now include additional data that lends support to the role of TANGO2 in lipid metabolism. We have changed the title accordingly.

1) The data with overexpressed TANGO2 looks convincing but I wonder if the authors analyzed the localization of endogenous TANGO2 by immunofluorescence using the antibody described in Figure S2. The idea that TANGO2 localizes to membrane contact sites between mitochondria and the ER and LDs would also be strengthened by experiments including multiple organelle markers.

We agree that most of the data on TANGO2 localization are based on the overexpression of the protein. As suggested by the reviewer and despite the lack of commercial antibodies for immunofluorescence-based evaluation, see the following chart, we tested the commercial antibody described in Figure 2 on HepG2 and U2OS cells. Moreover, we used Förster resonance energy transfer (FRET) technology to analyze the proximity of TANGO2 and Tom20, a specific outer mitochondrial membrane protein. In addition, we visualized cells expressing tagged TANGO2 and tagged VAP-B, an integral ER protein in the mitochondria-associated membranes (doi:10.1093/hmg/ddr559) or tagged TANGO2 and tagged GPAT4-Hairpin, an integral LD protein (doi:10.1016/j.devcel.2013.01.013). These data strengthen our proposal and are presented in the revised manuscript.

As suggested by the reviewer, we have also visualized two additional cell lines (HepG2 and U2OS) with the anti-TANGO2( from Novus Biologicals) that have been used for western blot (see chart above). As shown in the following figure, the commercial antibody shows a lot of staining in addition to mitochondria, especially in U2OS cells, where it also appears to label the nucleus.

2) The changes in LD size in TANGO2-depleted cells are very interesting and consistent with the role of TANGO2 in lipid metabolism. From the lipidomics analysis, it seems that the relative levels of the main neutral lipids in TANGO2-depleted cells remain unaltered (TAG) or even decrease (CE). Therefore, it would be interesting to explore further the increase in LD size for example analyze/display the absolute levels of neutral lipids in the various conditions.

We agree with the reviewer and now present the absolute levels of lipids of interest in the various conditions of the lipidomics analyses (Figure S 3).

3) Most of the lipidomics changes in TANGO2-depleted cells are observed in lipid species present in very low amounts while the relative abundance of major phospholipids (PC, PE PI) remains mostly unchanged. It would be good to also display the absolute levels of the various lipids analyzed. This is an important point to clarify as it would be unlikely that these major phospholipids are unaffected by an overall defect in Acyl-CoA metabolism, as proposed by the authors.

As stated above, we have now included the absolute levels of lipids of interest in the various conditions of the lipidomics analyses (Figure S 3).

Author Response

Reviewer #2 (Public Review):

I have only one concern with the study. I am not fully convinced that the disruption of behavioral updating is specifically due to NA signaling within OFC. In the first two studies, they observed non-specific anatomical effect likely due to the ablation of fibers of passage through OFC. The DREADD experiment is claimed to allay this concern. However, the DCZ was injected systemically. This means that any collaterals of LC NA neurons outside OFC will also be suppressed. While the lack of effect with the mPFC projection is interesting, this does not preclude an effect mediated in other target regions. Overall, I believe that none of the experiments truly demonstrate a specific effect of NA in OFC. A few experimental options that could be considered are injection of DCZ directly in OFC, optogenetic inhibition of fibers in OFC, or pharmacological disruption of NA signaling in OFC.

The other options are to measure the effect of the toxin ablations from experiments 1 and 2 not just in mPFC but in other regions. If the non-specific effect is truly only in mPFC outside of OFC, that would lead to more confidence that mPFC projection is the only other viable pathway mediating the effect.

As requested, we have quantified the effect of toxin ablations in neighbouring cortical regions known to be involved in the goal directed behavior, namely the insular cortex (IC, e.g., Balleine & Dickinson, 2000; Parkes & Balleine, 2013) the medial orbitofrontal cortex (MO, e.g., Bradfield et al., 2015; Gourley et al., 2016) and secondary motor cortex (M2, Gremel et al., 2016). Briefly, we found that injection of the saporin toxin in the VO and LO (Experiment 1) led to a significant decrease in NA fiber density in all examined regions. Injection of 6-OHDA also produced significant loss of NA fibres in MO and M2 but not insular cortex. These results are presented in Suppl. Figures 1 and 3 (pages 28 and 30) and the statistics are reported in the main text (page 6 and page 11)

We have also added the following to our discussion on the reason for the off-target depletions that we observed and acknowledged the potential role of collateral LC neurons:

Page 21, line starting 374: “The use of the saporin toxin led to a dramatic decrease of NA fiber density in all analysed cortical areas (Suppl Fig 1). This may be due to diffusion of the toxin from the injection site, the existence of collateral LC neurons and/or fibers passing through the ventral portion of the OFC but targeting other cortical areas (Cerpa et al 2019). However, injection of 6OHDA led to much less offsite NA depletion suggesting that a large part of the previous observation is toxin-specific. Indeed, no significant loss of NA fibers was visible in the insular cortex, which has been previously implicated in goal-directed behaviour (Balleine & Dickinson, 2000; Parkes et al., 2013; 2015; 2017). We did nevertheless observe an offsite depletion in more proximal prefrontal areas (prelimbic and medial orbitofrontal cortices) albeit a more modest depletion that what was observed using the saporin toxin. Several studies have described the projection pattern of LC cells. These studies, using various techniques, indicate that LC cells mainly target a single region, and that only a small proportion of LC neurons collateralize to minor targets (Plummer et al., 2020, Kebschull et al 2016, Uematsu et al 2017, Chandler et al 2014). Therefore, even if the OFC noradrenergic innervation is presumably specific (Chandler et al 2013), we cannot rule out a possible collateralization of some neurons toward neighbouring prefrontal areas (PL and MO). We have previously discussed that the posterior ventral portion of the OFC is an entry point for LC fibers en passant, which ultimately target other prefrontal areas (Cerpa et al 2019).

To achieve a greater anatomical selectivity we used a CAV-2 vector carrying the noradrenergic promoter PRS to target either the LC:A32 or the LC:OFC pathways (Hayat et al., 2020; Hirschberg et al., 2017). It has been shown that the CAV-2 vector can infect axons-of-passage, however the vector does not spread more than 200 µm from the injection site (Schwarz et al 2015). Therefore, when targeting the OFC we injected anteriorly to the level where the highest density of fibers of passage is expected (Cerpa et al 2019) in order to minimize infection of such fibers and restrict inhibition to our pathway of interest.

Overall, the current behavioural results are in line with our previous work showing that the ability to associate new outcomes to previously acquired actions is impaired following chemogenetic inhibition of the VO and LO (Parkes et al., 2018) or disconnection of the VO and LO from the submedius thalamic nucleus (Fresno et al 2019). These results point to a necessary role of the ventral and lateral parts of the OFC and its noradrenergic innervation for updating A-O associations. However, it is worth mentioning that different subregions of the OFC, both along the medio-lateral and antero-posterior axes of OFC, display clear functional heterogeneities (Dalton et al 2016, Izquierdo 2017, Panayi & Killcross, 2018, Bradfield et al 2018, Barreiros et al 2021). Therefore, while we have previously focused on the anatomical heterogeneity of the noradrenergic innervation in these prefrontal subregions (Cerpa et al 2019), a thorough characterization of its functional role in each of these subregions still needs to be addressed.”

One last concern is that the lack of the effect due to disruption of the mPFC projection is not guaranteed to not be from experimental issues. If the authors have some evidence that the mPFC projection disruption produced some other behavioral effect, that would make the lack of effect in this case more convincing.

Unfortunately, we do not provide evidence in the current paper that disrupting the LC:mPFC (now termed LC:A32 in the current study, based on the recommendation of reviewer 1) projection produces some other behavioural effect. However, in an on-going series of experiments, using the same tools as the current study, we found that inhibiting the LC:A32, but not LC:OFC, pathway impairs Pavlovian contingency degradation as shown in the figure below. We therefore believe that the failure of LC:mPFC pathway inhibition to effect outcome identity reversal in the present study is not due to experimental issues. Please note that in the figure below mPFC is referred to as area 32 (A32), as requested by reviewer 1.

Figure 1. A) Experimental timeline for the Pavlovian contingency degradation procedure. Prior to behavioural training, rats were injected with CAV2-PRS-hM4D-mCherry into either the vlOFC or area 32 (A32). Number of food port entries during the non-degraded CS and degraded CS for rats injected with vehicle and rats injected with DCZ during degradation training (B, D) and the test in extinction (C, E). Inhibition of the LC:vlOFC had no effect on Pavlovian contingency degradation, whereas inhibition of LC:A32 during degradation training rendered rats insensitive to the change in the causal relationship between the CS and the US.

Reviewer #3 (Public Review):

I would be curious about the authors' thoughts regarding the recent Duan ... Robbins Neuron paper (https://pubmed.ncbi.nlm.nih.gov/34171290/), in which marmosets displayed paradoxical responses to VLO inactivation and stimulation in contingency degradation tasks. Are there ways to reconcile these reports?

We previously argued that the updating processes underlying changes in causal contingency versus outcome identity may be supported by different prefrontal regions (Cerpa et al., 2021, Behav Neurosci). Unfortunately, the tasks used in the current study do not allow us to test if our rats are sensitive to changes in the action-outcome contingency. In fact, the effect of inactivation (or overactivation) of the ventral and lateral regions of OFC on an instrumental contingency degradation task similar to that used in Duan et al (2022) has not yet been examined in rats.

Indeed, while it is stated in Duan et al (2022) that rats with lesions of lateral OFC are insensitive to contingency degradation, none of the citations provided support this conclusion (Balleine & Dickinson, 1998; Corbit & Balleine, 2003; Ostlund and Balleine, 2007; Yin et al., 2005). Balleine and Dickinson (1998) assessed the effect of prelimbic and insular cortex lesions (insular anteroposterior coordinate +1.2), with only the former affecting instrumental contingency degradation. Ostlund and Balleine (2007) assessed the effect of orbitofrontal lesions on Pavlovian contingency degradation (degradation of the S-O contingency) not instrumental contingency degradation. Finally, Corbit and Balleine (2003) and Yin et al (2005) assessed the effect of prelimbic and dorsomedial striatum lesions, respectively. Nevertheless, there are some reports on the effect of chemogenetic inhibition of VO/LO on degradation in a nose-poke response task but the results are conflicting (e.g., Whyte et al., 2019; Zimmerman et al., 2017; 2018). It would be very interesting to study the impact of both inactivation and overactivation of VO and LO in rats to compare with the results found in marmosets, using comparable tasks.

We have added the following to our discussion, which cites Duan et al (2022) and the need to better understand the role of VO and LO in contingency degradation.

Page 24, line starting 450: “However, it is not yet clear if the NA-OFC system is also involved in detecting the causal relationship between an action and its outcome (see Cerpa et al., 2021 for a discussion). Some have reported impaired adaptation to contingency changes following inhibition of VO and LO or BDNF-knockdown in these regions (Whyte et al., 2019; Zimmerman et al., 2017), while another study shows that inhibition of VO/LO leaves sensitivity to degradation intact, at least during an initial test (Zimmerman et al., 2018). Interestingly, a recent paper in marmosets demonstrates that inactivation of anterior OFC (area 11) improves instrumental contingency degradation, whereas overactivation impairs degradation (Duan et al., 2022). The potential role of the rodent ventral and lateral regions of OFC, and the NA innervation of OFC, in adapting to degradation of instrumental contingencies requires further investigation.”

Author Response:

Reviewer #1 (Public Review):

There is growing precedent for the utility of GWAS-type analyses in elucidating otherwise cryptic genotypic associations with specific Mtb phenotypes, most commonly drug resistance. This study represents the latest instalment of this type of approach, utilizing a large set of WGS data from clinical Mtb isolates and refining the search for DR-associated alleles by restricting the set to those predicted (or known) to be phenotypically DR. This revealed a number of potential candidate mutations, including some in nucleotide excision repair (uvrA, uvrB), in base excision repair (mutY), and homologous recombination (recF). In validating these leads functional assays, the authors present evidence supporting the impact of the identified mutations on antibiotic susceptibility in vitro and in macrophage and animal infection models. These results extend the number of candidate mutations associated with Mtb drug resistance, however the following must be considered:

(i) The GWAS analysis is the basis of this study, yet the description of the approach used and presentation of results obtained is occasionally obscure; for example, the authors report the use of known drug resistance phenotypes (where available) or inferences of drug-resistance from genotypic data to enhance the potential to identify other mutations that might be implicated in enabling the DR mutations, yet their list of known DR mutations seem to be predominantly rare or unusual mutations, not those commonly associated with clinical DR-TB. In addition, the distribution of the identified resistance-associated mutations across the different lineages need to be explained more clearly.

In the revised manuscript, we have performed the phylogenetic analysis of the strains used. A phylogenetic tree was generated using Mycobacterium canetti as an outgroup (Figure 1b). The phylogeny analysis suggests the clustering of the strains in lineage 1, 2, 3, and 4. Lineages 2,3 and 4 are clustering together, and lineage 1 is monophyletic, as reported previously. The genome sequence data of 2773 clinical strains were downloaded from NCBI. These strains were also part of the GWAS analysis performed by Coll et al (https://pubmed.ncbi.nlm.nih.gov/29358649/) and Manson et al. (https://pubmed.ncbi.nlm.nih.gov/28092681/). The phenotype of the strains used for the association analysis was reported in the previous studies. We have not performed other predictions. The supplementary table provides the lineage origin of each strain used in the study (Supplementary File 1 & 2). The distributions of resistance-associated mutations in different strains is shown (Figure 2-figure supplement 6a-h). As suggested, we have performed an analysis wherein we looked for the direct target mutations that harbor mutations in the DNA repair genes (Figure 2-figure supplement 6i-k).

We identified mostly the rare mutations due to the following reasons;

1. We looked for the mutations that were present only in the multidrug resistant strains as compared to the susceptible strains for association mapping. This strategy exclusively gave most variants associated with multidrug resistant phenotype.

2. We have used Mixed Linear Model (MLM) for association analysis. MLM removes all the population-specific SNPs based on PCA and kinship corrections. The false discovery rate (FDR) adjusted p-values in the GAPIT software are stringent as it corrects the effects of each marker based on the population structure (Q) as well as kinship (K) values. Therefore the probability of identifying the false-positive SNP is very low. We combined it with the Bonferroni corrections to identify markers associated with the drug resistant phenotype.

(ii) By combining target gene deletions with different complementation alleles, the authors provide compelling microbiological evidence supporting the inferred role of the mutY and uvrB mutations in enhanced survival under antibiotic treatment. The experimental work, however, is limited to assessments of competitive survival in various models, with/without antibiotic selection, or to mutant frequency analyses; there is no direct evidence provided in support of the proposed mechanism.

To ascertain if the better survival of the RvDmutY, or RvDmutY::mutY-R262Q, is indeed due to the acquisition of mutations in the direct target of antibiotics, we performed WGS of the strain from the ex vivo evolution experiment (Figure 5). Genomic DNA extracted from ten independent colonies (grown in vitro), was mixed in equal proportions before library preparation. Only those SNPs present in >20% of reads were retained for the analysis. Analysis of Rv sequences grown in vitro suggested that the laboratory strain has accumulated 100 SNPs compared with the reference strain. The sequence of Rv laboratory strain was used as the reference strain for the subsequent analysis. WGS data for RvDmutY, RvDmutY::mutY, and RvDmutY::mutY-R262Q strains grown in vitro did not show the presence of a mutation in the antibiotic target genes. In a similar vein, ten independent colonies, each from the 7H11-OADC plates, after the final round of ex vivo selection in the presence or absence of antibiotics, were selected for WGS. Data indicated that in the absence of antibiotics, no direct target mutations were identified in the ex vivo passaged strains (Figure 6a & e). In the presence of isoniazid, we found mutations in the katG (Ser315Thr or Ser315Ileu) in the Rv, RvDmutY but not in RvDmutY:mutY and RvDmutY::mutY-R262Q (Figure 6b & e). These findings are in congruence with the ex vivo evolution CFU analysis, wherein we did not observe a significant increase in the survival of RvDmutY and RvDmutY::mutY R262Q in the presence of isoniazid (Figure 5). In the presence of ciprofloxacin and rifampicin, direct target mutations were identified in the gyrA and rpoB (Figure 6c e). Asp94Glu/Asp94Gly mutations were identified in gyrA, and, His445Tyr/Ser450Leu mutations were identified in rpoB of RvDmutY and RvDmutY::mutY-R262Q, respectively. No direct target mutations were identified in the Rv and RvDmutY::mutY, suggesting that the perturbed DNA repair aids in acquiring the drug resistance-conferring mutations in Mtb (Figure 6c-e & Supplementary File 8).

To determine if the better survival of the RvDmutY, or RvDmutY::mutY-R262Q, in the guinea pig infection experiment (Figure 8) is due to the accumulation of mutations in the host, we performed WGS of the strain isolated from guinea pig lungs. Analysis revealed specific genes such as cobQ1, smc, espI, and valS were mutated only in RvDmutY and RvDmutY::mutYR262Q but not in Rv and RvDmutY::mutY. Besides, tcrA and gatA were mutated only in RvDmutY, whereas rv0746 were mutated exclusively in the RvDmutY:mutY (Figure 8-Figure Supplement 2). However, we did not observe any direct target mutations; this may be because guinea pigs were not subjected to antibiotic treatment. Data suggests that the continued longterm selection pressure is necessary for bacilli to acquire mutations.

(iii) The low drug concentrations used (especially of rifampicin against M. smegmatis) suggest the identified mutations confer low-level resistance to multiple antimycobacterial agents - in turn implying tolerance rather than resistance. If correct, it would be interesting to know how broadly tolerant strains containing these mutations are; that is, whether susceptibility is decreased to a broad range of antibiotics with different mechanisms of action (including both cidal and static agents), and whether the extent of the decrease be determined quantitatively (for example, as change in MIC value).

To evaluate the effect of different drugs on the survival of RvDmutY or RvDmutY::mutYR262Q, we performed killing kinetics in the presence and absence of isoniazid, rifampicin, ciprofloxacin, and ethambutol (Figure 4a). In the absence of antibiotics, the growth kinetics of Rv, RvDmutY, RvDmutY:mutY, and RvDmutY::mutY-R262Q were similar (Figure 4b). In the presence of isoniazid, ~2 log-fold decreases in bacterial survival was observed on day 3 in Rv and RvDmutY:mutY; however, in RvDmutY and RvDmutY::mutY-R262Q, the difference was limited to ~1.5 log-fold (Figure 4c). A similar trend was apparent on days 6 and 9, suggesting a ~5-fold increase in the survival of RvDmutY and RvDmutY::mutY-R262Q compared with Rv and RvDmutY:mutY (Figure 4c). Interestingly, in the presence of ethambutol, we did not observe any significant difference (Figure 4d). In the presence of rifampicin and ciprofloxacin, we observed a ~10-fold increase in the survival of RvDmutY and RvDmutY::mutY-R262Q compared with Rv and RvDmutY:mutY (Figure 4e-f). Thus results suggest that the absence of mutY or the presence of mutY variant aids in subverting the antibiotic stress.

Reviewer #2 (Public Review):

This interesting manuscript uses a collection of whole genome sequences of TB isolates to associate specific sequence polymorphisms with MDR/XDR strains, and having found certain mutations in DNA repair pathways, does a detailed analysis of several mutations. The evaluation of the MutY polymorphism reveals it is loss of function and TB strains carrying this mutation have a higher mutation frequency and enhanced survival in serial passage in macrophages. The strengths of the manuscript are the leveraging of a large sequence dataset to derive interesting candidate mutations in DNA repair pathway and the demonstration that at least one of these mutations has a detectable effect on mutagenicity and pathogenesis. The weaknesses of the manuscript are a lack of experimental exploration of the mechanism by which loss of a DNA repair pathway would enhance survival in vivo. The model presented is that these phenotypes are due to hypermutagenicity and thereby evolution of enhanced pathogenesis, but this is not actually directly tested or investigated. There are also some technical concerns for some of the experimental data which can be strengthened.

This paper presents the following data:

• Analyzed whole-genome sequences 2773 clinical strains: 160 000 SNPs identified
• 1815 drug-susceptible/422 MDR/XDR strains: 188 mutations correlated with Drug resistance.
• Novel mutations associated with the drug resistance have been found in base excision repair (BER), nucleotide excision repair (NER), and homologous recombination (HR) pathway genes (mutY, uvrA, uvrB, and recF).
• Specific mutations mutY-R262Q and uvrB-A524V were studied.
• mutY-R262Q and uvrB-A524V mutations behave as loss of function alleles in vivo, as measured by non-complementation of the increased mutation frequency measured by resistance to Rif and INH.
• The mutY deletion and the mutY-R262Q mutation increase Mtb survival over WT in macrophages when Mtb has not been submitted to previous rounds of macrophage infection.
• This advantage is exacerbated in presence of antibiotic (Rif and Cipro but not INH).
• The MutY deletion and the MutY-R262Q mutation result in an enhanced survival of Mtb during guinea pig infection.

Major issues:

The finding that mutations in MutY confers an advantage during macrophage infection is convincing based on the macrophage experiments, but it is premature to conclude that the mechanism of this effect is due to hypermutagenesis and selection of fitter bacterial clones. It is described in E. coli (Foti et al., 2012) and recently in mycobacteria (Dupuy et al., 2020) that the MutY/MutM excision pathways can increase the lethality of antibiotic treatment because of double-strand breaks caused by Adenine/oxoG excisions. The higher survival of the mutY mutant during antibiotic treatment could more be due to lower Adenine/oxoG excision in the mutant rather than acquisition of advantageous mutations, or some other mechanism. The same hypothesis cannot be excluded for the Guinea pig experiments (no antibiotics, but oxidative stress mediated by host defenses could also increase oxoG) and should at least be discussed. Experiments that would support the idea that the in vivo advantage is due to hypermutagenesis would be whole genome sequencing of the output vs input populations to directly document increased mutagenesis. Similarly, is the ΔmutY survival advantage after rounds of macrophage infections dependent on macrophage environment? What happens if the ΔmutY strain is cultivated in vitro in 7H9 (same number of generations) before infecting macrophages?

We thank the reviewer for the insightful comments. To ascertain if the better survival of the RvDmutY, or RvDmutY::mutY-R262Q, is indeed due to the acquisition of mutations in the direct target of antibiotics, we performed WGS of the strain from the ex vivo evolution experiment (Figure 5). Genomic DNA extracted from ten independent colonies (grown in vitro) was mixed in equal proportion prior to library preparation. For the analysis, only those SNPs that were present in >20% of reads were retained. Analysis of Rv sequences grown in vitro suggested that the laboratory strain has accumulated 100 SNPs compared with the reference strain. The sequence of the Rv laboratory strain was used as the reference strain for the subsequent analysis. WGS data for RvDmutY, RvDmutY::mutY, and RvDmutY::mutY-R262Q strains grown in vitro did not show the presence of a mutation in the antibiotic target genes. In a similar vein, ten independent colonies, each from the 7H11-OADC plates, after the final round of ex vivo selection in the presence or absence of antibiotics, were selected for WGS. Data indicated that in the absence of antibiotic, no direct target mutations were identified in the ex vivo passaged strains (Figure 6a & e). In the presence of isoniazid, we found mutations in the katG (Ser315Thr or Ser315Ileu) in the Rv, RvDmutY but not in RvDmutY:mutY and RvDmutY::mutY-R262Q (Figure 6b & e). These findings are in congruence with the ex vivo evolution CFU analysis, wherein we did not observe a significant increase in the survival of RvDmutY and RvDmutY::mutY R262Q in the presence of isoniazid (Figure 5). In the presence of ciprofloxacin and rifampicin, direct target mutations were identified in the gyrA and rpoB (Figure 6c-e). Asp94Glu/Asp94Gly mutations were identified in gyrA, and, His445Tyr/Ser450Leu mutations were identified in rpoB of RvDmutY and RvDmutY::mutY-R262Q, respectively. No direct target mutations were identified in the Rv and RvDmutY::mutY, suggesting that the perturbed DNA repair aids in acquiring the drug resistance-conferring mutations in Mtb (Figure 6c-e & Supplementary File 8).

To determine if the better survival of the RvDmutY, or RvDmutY::mutY-R262Q, in the guinea pig infection experiment (Figure 8) is due to the accumulation of mutations in the host, we performed WGS of the strain isolated from guinea pig lungs. Analysis revealed specific genes such as cobQ1, smc, espI, and valS were mutated only in RvDmutY and RvDmutY::mutYR262Q but not in Rv and RvDmutY::mutY. Besides, tcrA and gatA were mutated only in RvDmutY, whereas rv0746 were mutated exclusively in the RvDmutY:mutY (Figure 8-figure supplement 2). However, we did not observe any direct target mutations; this may be because guinea pigs were not subjected to antibiotic treatment. Data suggests that the continued longterm selection pressure is necessary for bacilli to acquire mutations.

• It would be useful to present more data about the strain relatedness and genome characteristics of the DNA repair mutant strains in the GWAS. For example, the model would suggest that strains carrying DNA repair mutations should have higher SNP load than control strains. Additionally, it would be helpful to know whether the identified DNA repair pathway mutations are from epidemiologically linked strains in the collection to deduce whether these events are arising repeatedly or are a founder effect of a single mutant since for each mutation, the number of strains is small.

We analyzed the genome of the clinical strains that possess DNA repair gene mutations to determine the additional polymorphisms. The number of SNPs in the strains harboring DNA repair mutation and the drug susceptible strains appears to be similar. The marginal difference, if any were not statistically significant.

We agree with the reviewer that these strains might be epidemiologically linked. In the present study, all the strains harboring mutation in mutY belong to lineage 4. We observed that all the mutY mutationcontaining strains were either MDR or pre-XDR compared with drug susceptible strains of the same clade.

• Some of the mutation frequency, survival and competition data could be strengthened by more experimental replicates. Data Lines 370-372 (mutation frequency), lines 387-388 (Survival of strains ex vivo), line 394 (competition experiment) : "Two biologically independent experiments were performed. Each experiment was performed in technical triplicates. Data represent one of the two biological experiments." Two biological replicates is insufficient for the phenotypes presented and all replicates should be included in the analysis. In addition, the definition of "technical triplicates" should be given, does this mean the same culture sampled in triplicate?

We thank the reviewer for the comment. We performed at least two independent experiments with biological triplicates (not technical triplicates). We apologize for writing this incorrectly. We have reported data from one independent experiment consisting of at least biological triplicates. For mutation rate analysis, we have performed experiment using six independent colonies. These points are mentioned in the methods and legends of the revised manuscript.

• MutY phenotypes. One caveat to the conclusion that the MutY R262Q mutant is nonfunctional is the lack of examination of the expression of the complementing protein. I would be informative to comment on the location of this mutation in relation to the known structures of MutY proteins. Similarly, for the UvrB polymorphism, this null strain has a clear UV sensitivity phenotype in the literature, so a fuller interrogation for UV killing would be informative re: the A524V mutation.

We have now included the western blot data on both complementation strains (Figure 3-figure supplement 1). We agree with the reviewer that the uvrB null mutant may have UV sensitivity phenotype, but we have not performed the experiment in the present study.

Reviewer #3 (Public Review):

STRENGTHS

• This ambitious study is broad in scope, beginning with a bacterial GWAS study and extending all the way to in vivo guinea pig infection models.

• Numerous reports have attempted to identify Mtb strains with elevated mutation rates, and the results are conflicting. The present study sets out to thoroughly evaluate one such mutation that may produce a mutator phenotype, mutY-Arg262Gln.

WEAKNESSES

• While the authors follow-up experiments with the mutY-Arg262Gln allele are all consistent with the conclusion that this mutation elevates the mutation rate in Mtb and thus could promote the evolution of drug resistance, further work is needed to unambiguously demonstrate this link.

• The authors highlight five mutations in genes associated with DNA replication and or repair from their GWAS analysis:

o dnaA-Arg233Gln: as the authors note in the Discussion, Hicks et al. associate SNPs in dnaA with low-level isoniazid resistance, as a result of lowered katG expression. Since this is unrelated to their focus on DNA repair genes whose mutation could elevate mutation rates, I would consider removing this allele from the Table.

As suggested, we have removed the dnaA from Table 3.

o mutY-Arg262Gln: querying publicly available whole genome sequences of clinical Mtb isolates, this SNP appears to be restricted to lineage 4.3 (L4.3). All of these L4.3 strains appear to be drug-resistant. How many times did the mutY-Arg262Gln mutation evolve in the authors dataset? If there is evidence of homoplastic evolution, this would strengthen their case. If not, it doesn't mean the authors findings are incorrect, but does elevate that risk that this mutation could be a passenger (i.e. not driver) mutation. To address this, the authors could attempt to date when the mutY-Arg262Gln arose. If it was before the evolution of drug-resistance conferring alleles in these L4.3 strains, that is consistent with (but not proof of) a driver mutation. If mutY-Arg262Gln arose after, this is much more consistent with a passenger mutation.

As pointed out by the reviewer, the mutY-Arg262Gln mutation is restricted to lineage 4. We have checked the mutY gene sequence from the strains harboring mutY Arg262Gln mutation and sensitive strains of the same clade. We identified only the reported mutation in the drug-resistant strains, and there was no synonymous mutation that could be used for performing molecular clock analysis. To ascertain whether it is a passenger or a driver mutation, we have performed multiple experiments that suggest that identified mutation aids in the acquisition of drug resistance.

o uvrB-Ala524Val: curiously we don't see this SNP in our dataset of publicly available whole genome sequences of clinical Mtb isolates (~45,000 genomes).

We have rechecked this SNP in our dataset. This SNP was present in 87 drug-resistant strains that belong to lineage 2.

o uvrA-Gln135Lys: this SNP also appears to be restricted to lineage 4.3. Same question as for mutY-Arg262Gln.

As pointed out by the reviewer, uvrA-Gln135lys mutation is restricted to lineage 4. We identified only the reported mutation in the drug-resistant strains, and there was no synonymous mutation that can be used for performing molecular clock analysis

o recF-Gly269Gly: this is a very common mutation, is it unique to lineage 2.2.1? Same question as for mutY-Arg262Gln.

RecF-Gly269Gly mutation was present in the lineage 2 strains. Here also, we identified only the reported mutation in the drug-resistant strains, and there was no synonymous mutation could be used for performing molecular clock analysis.

• The CRYPTIC consortium recently published a number of preprints on biorxiv detailing very large GWAS studies in Mtb. Did any of these reports also associate drug resistance with mutY? If yes, this should be stated. If not, the potential reasons for this discrepancy should be discussed.

We have checked the recently published CRYPTIC consortium article (https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.3001721#sec012) for mutY-Arg262Gln. We did not find the mutY-Arg262Gln mutation in their analysis; this is due to the different strains used in the study. However, we identified recF Gly269Gly mutation in their datase

• Based on the authors follow-up studies in vivo, MutY-Arg262Gln is presumed to be a loss-of-function allele. If the authors could convincingly demonstrate this biochemically with recombinant proteins, this would significantly strengthen their case.

Experiments performed in Msm and Mtb mutant strains suggest that MutY variant is a loss-of-function allele. We have not performed in vitro assays to confirm the same.

• If the authors are correct and mutY-Arg262Gln strains have elevated mutation rates, presumably there would be evidence of this in the clinical strain sequencing data. Do mutY-Arg262Gln containing strains have elevated C→G or C→A mutations in their genomes? Presumably such strains would also have a higher number of SNPs than closely related strains WT for mutY- is this the case?

We analyzed the genome of the clinical strains that possess DNA repair gene mutations to determine the additional polymorphisms. The number of SNPs in the strains harboring DNA repair mutation and the drug susceptible strains appears to be higher. We have also looked for the CàT and CàG mutations in the same strains. CàT mutations are higher in the strains harboring mutY variant compared with the susceptible strains (Figure 2-figure supplement 6 l). However, we could not perform statistical analysis as the number of strains that harbor mutY variant is limited to 8. Thus data suggest that empirically the strains harboring mutY variant show higher SNPs elsewhere and CàT mutations. We are not stating these conclusions strongly in the manuscript as the data is not statistically significant

• While more work, mutation rates as measured by Luria-Delbruck fluctuation analysis are more accurate than mutation frequencies. I would recommend repeating key experiments by Luria-Delbruck fluctuation analysis. It is also important to report both drug-resistant colony counts and total CFU in these sorts of experiments. Given the clumpy nature of mycobacteria, mutation rates can appear to be artificially elevated due to low total CFU and not an increase in the number of drug-resistant colonies.

As suggested, we determined the mutation rate in the presence of isoniazid, rifampicin, and ciprofloxacin (Figure 3g-j). The fold increase in the mutation rate relative to Rv for RvDmutY, RvDmutY:mutY, and RvDmutY::mutY-R262Q was 2.90, 0.76, and 3.0 in the presence of isoniazid and 5.62, 1.13, and 5.10 or 9.14, 1.57, and 8.71 in the presence of rifampicin and ciprofloxacin respectively (Figure 3).

• Figure 4 would appear to measuring drug tolerance not resistance? Are the elevated CFU in the presence of drugs in the mutY-Arg262Gln strain due to an increase in the number of drug resistant strains or drug sensitive strains? This could be assessed by quantifying resulting CFU in the presence or absence the indicated drugs.

To ascertain better survival is due to the acquisition of mutations in the direct target of antibiotics or drug tolerance. We performed WGS of the strain from the ex vivo evolution experiment (Figure 5). Genomic DNA extracted from ten independent colonies (grown in vitro) was mixed in equal proportion prior to library preparation. Only those SNPs present in >20% of reads were retained for the analysis. Analysis of Rv sequences grown in vitro suggested that the laboratory strain has accumulated 100 SNPs compared with the reference strain. The sequence of the Rv laboratory strain was used as the reference strain for the subsequent analysis. WGS data for RvDmutY, RvDmutY::mutY, and RvDmutY::mutY-R262Q strains grown in vitro did not show the presence of a mutation in the antibiotic target genes. In a similar vein, ten independent colonies, each from the 7H11-OADC plates, after the final round of ex vivo selection in the presence or absence of antibiotics, were selected for WGS. Data indicated that in the absence of antibiotics, no direct target mutations were identified in the ex vivo passaged strains (Figure 6a & e). In the presence of isoniazid, we found mutations in the katG (Ser315Thr or Ser315Ileu) in the Rv, RvDmutY but not in RvDmutY::mutY and RvDmutY::mutY-R262Q (Figure 6b & e). These findings are in congruence with the ex vivo evolution CFU analysis, wherein we did not observe a significant increase in the survival of RvDmutY and RvDmutY::mutY-R262Q in the presence of isoniazid (Figure 5). In the presence of ciprofloxacin and rifampicin, direct target mutations were identified in the gyrA and rpoB (Figure 6c-e). Asp94Glu/Asp94Gly mutations were identified in gyrA, and, His445Tyr/Ser450Leu mutations were identified in rpoB of RvDmutY and RvDmutY::mutY-R262Q, respectively. No direct target mutations were identified in the Rv and RvDmutY::mutY, suggesting that the perturbed DNA repair aids in acquiring the drug resistance-conferring mutations in Mtb (Figure 6c-e & Supplementary File 8).

To determine if the better survival of the RvDmutY, or RvDmutY::mutY-R262Q, in the guinea pig infection experiment (Figure 8) is due to the accumulation of mutations in the host, we performed WGS of the strain isolated from guinea pig lungs. Analysis revealed specific genes such as cobQ1, smc, espI, and valS were mutated only in RvDmutY and RvDmutY::mutYR262Q but not in Rv and RvDmutY::mutY. Besides, tcrA and gatA were mutated only in RvDmutY, whereas rv0746 were mutated exclusively in the RvDmutY::mutY (Figure 2-figure supplement 6). However, we did not observe any direct target mutations; this may be because guinea pigs were not subjected to antibiotic treatment. Data suggests that the continued longterm selection pressure is necessary for bacilli to acquire mutations.

Author Response

Reviewer #3: (Public Review):

In this ms Li et al. examine the molecular interaction of Rabphilin 3A with the SNARE complex protein SNAP25 and its potential impact in SNARE complex assembly and dense core vesicle fusion.

Overall the literature of rabphilin as a major rab3/27effector on synaptic function has been quite enigmatic. After its cloning and initial biochemical analysis, rather little new has been found about rabphilin, in particular since loss of function analysis has shown rather little synaptic phenotypes (Schluter 1999, Deak 2006), arguing against that rabphilin plays a crucial role in synaptic function.

While the interaction of rabphilin to SNAP25 via its bottom part of the C2 domain has been already described biochemically and structurally in the Deak et al. 2006, and others, the authors make significant efforts to further map the interactions between SNAP25 and rabphilin and indeed identified additional binding motifs in the first 10 amino acids of SNAP25 that appear critical for the rabphilin interaction.

Using KD-rescue experiments for SNAP25, in TIRF based imaging analysis of labeled dense core vesicles showed that the N-terminus of SN25 is absolutely essential for SV membrane proximity and release. Similar, somewhat weaker phenotypes were observed when binding deficient rabphilin mutants were overexpressed in PC12 cells coexpressing WT rabphilin. The loss of function phenotypes in the SN25 and rabphilin interaction mutants made the authors to claim that rabphilin-SN25 interactions are critical for docking and exocytosis. The role of these interaction sites were subsequently tested in SNARE assembly assays, which were largely supportive of rabphilin accelerating SNARE assembly in a SN25 -terminal dependent way.

Regarding the impact of this work, the transition of synaptic vesicles to form fusion competent trans-SNARE complex is very critical in our understanding of regulated vesicle exocytosis, and the authors put forward an attractive model forward in which rabphilin aids in catalyzing the SNARE complex assembly by controlling SNAP25 a-helicalicity of the SNARE motif. This would provide here a similar regulatory mechanism as put forward for the other two SNARE proteins via their interactions with Munc18 and intersection, respectively.

We thank the reviewer #3 for the summary of the paper and for the praise of our work. The point-to-point replies are as follow:

While discovery of the novel interaction site of rabphilin with the N-Terminus of SNAP25 is interesting, I have issues with the functional experiments. The key reliance of the paper is whether it provides convincing data on the functional role of the interactions, given the history of loss of function phenotypes for Rabphilin. First, the authors use PC12 cells and dense core vesicle docking and fusion assays. Primary neurons, where rabphilin function has been tested before, has unfortunately not been utilized, reducing the impact of docking and fusion phenotype.

We have discussed these questions as mentioned in our response to Essential Revisions 3 and added this corresponding passage to the Discussion section (pp.18-19, lines 407-427).

In particular the loss of function phenotype in figure 3 of the n-terminally deleted SNAP25 in docking and fusion is profound, and at a similar level than the complete loss of the SNARE protein itself. This is of concern as this is in stark contrast to the phenotype of rabphilin loss in mammalian neurons where the phenotype of SNAP25 loss is very severe while rabphilin loss has almost no effect on secretion. This would argue that the N-terminal of SNAPP25 has other critical functions besides interacting with rabphilin. In addition, it could argue that the n-Terminal SNAP25 deletion mutant may be made in the cell (as indicated from the western blot) but may not be properly trafficked to the site of release

To test whether the N-peptide deletion mutant of SN25 can properly target to the plasma membrane, we overexpressed the SN25 FL or SN25 (11–206) with C-terminal EGFP-tag in PC12 cells and monitored the localization of SN25 FL-EGFP and SN25 (11–206)-EGFP near the plasma membrane by TIRF microscopy. We observed that the average fluorescence intensity of SN25 (11–206)-EGFP showed no significant difference with SN25 FL-EGFP as below, suggesting that the N-peptide deletion mutant may not influence the trafficking of SN25 to plasma membrane.

(A) TIRF imaging assay to monitor the localization of SN25-EGFP near the plasma membrane. Overexpression of SN25 FL-EGFP (left) and SN25 (11–206)-EGFP (right) using pEGFP-N3 vector in PC12 cells. Scale bars, 10 μm. (B) Quantification of the average fluorescence intensity of SN25-EGFP near the plasma membrane in (A). Data are presented as mean ± SEM (n ≥ 10 cells in each). Statistical significance and P values were determined by Student’s t-test. ns, not significant.

Author Response

Reviewer #1 (Public Review):

The authors present a PyTorch-based simulator for prosthetic vision. The model takes in the anatomical location of a visual cortical prostheses as well as a series of electrical stimuli to be applied to each electrode, and outputs the resulting phosphenes. To demonstrate the usefulness of the simulator, the paper reproduces psychometric curves from the literature and uses the simulator in the loop to learn optimized stimuli.

One of the major strengths of the paper is its modeling work - the authors make good use of existing knowledge about retinotopic maps and psychometric curves that describe phosphene appearance in response to single-electrode stimulation. Using PyTorch as a backbone is another strength, as it allows for GPU integration and seamless integration with common deep learning models. This work is likely to be impactful for the field of sight restoration.

1) However, one of the major weaknesses of the paper is its model validation - while some results seem to be presented for data the model was fit on (as opposed to held-out test data), other results lack quantitative metrics and a comparison to a baseline ("null hypothesis") model. On the one hand, it appears that the data presented in Figs. 3-5 was used to fit some of the open parameters of the model, as mentioned in Subsection G of the Methods. Hence it is misleading to present these as model "predictions", which are typically presented for held-out test data to demonstrate a model's ability to generalize. Instead, this is more of a descriptive model than a predictive one, and its ability to generalize to new patients remains yet to be demonstrated.

We agree that the original presentation of the model fits might give rise to unwanted confusion. In the revision, we have adapted the fit of the thresholding mechanism to include a 3-fold cross validation, where part of the data was excluded during the fitting, and used as test sets to calculate the model’s performance. The results of the cross- validation are now presented in panel D of Figure 3. The fitting of the brightness and temporal dynamics parameters using cross-validation was not feasible due to the limited amount of quantitative data describing temporal dynamics and phosphene size and brightness for intracortical electrodes. To avoid confusion, we have adapted the corresponding text and figure captions to specify that we are using a fit as description of the data.

We note that the goal of the simulator is not to provide a single set of parameters that describes precise phosphene perception for all patients but that it could also be used to capture variability among patients. Indeed, the model can be tailored to new patients based on a small data set. Figure 3-figure supplement 1 exemplifies how our simulator can be tailored to several data sets collected from patients with surface electrodes. Future clinical experiments might be used to verify how well the simulator can be tailored to the data of other patients.

Specifically, we have made the following changes to the manuscript:

• Caption Figure 2: the fitted peak brightness levels reproduced by our model

• Caption Figure 3: The model's probability of phosphene perception is visualized as a function of charge per phase

• Caption Figure 3: Predicted probabilities in panel (d) are the results of a 3-fold cross- validation on held-out test data.

• Line 250: we included biologically inspired methods to model the perceptual effects of different stimulation parameters

• Line 271: Each frame, the simulator maps electrical stimulation parameters (stimulation current, pulse width and frequency) to an estimated phosphene perception

• Lines 335-336: such that 95% of the Gaussian falls within the fitted phosphene size.

• Line 469-470: Figure 4 displays the simulator's fit on the temporal dynamics found in a previous published study by Schmidt et al. (1996).

• Lines 922-925: Notably, the trade-off between model complexity and accurate psychophysical fits or predictions is a recurrent theme in the validation of the components implemented in our simulator.

2) On the other hand, the results presented in Fig. 8 as part of the end-to-end learning process are not accompanied by any sorts of quantitative metrics or comparison to a baseline model.

We now realize that the presentation of the end-to-end results might have given the impression that we present novel image processing strategies. However, the development of a novel image processing strategy is outside the scope of the study. Instead, The study aims to provide an improved simulation which can be used for more realistic assessment of different stimulation protocols. The simulator needs to fit experimental data, and it should run fast (so it can be used in behavioral experiments). Importantly, as demonstrated in our end-to-end experiments, the model can be used in differentiable programming pipelines (so it can be used in computational optimization experiments), which is a valuable contribution in itself because it lends itself to many machine learning approaches which can improve the realism of the simulation.

We have rephrased our study aims in the discussion to improve clarity.

• Lines 275-279: In the sections below, we discuss the different components of the simulator model, followed by a description of some showcase experiments that assess the ability to fit recent clinical data and the practical usability of our simulator in simulation experiments

• Lines 810-814: Computational optimization approaches can also aid in the development of safe stimulation protocols, because they allow a faster exploration of the large parameter space and enable task-driven optimization of image processing strategies (Granley et al., 2022; Fauvel et al., 2022; White et al., 2019; Küçükoglü et al. 2022; de Ruyter van Steveninck et al., 2022; Ghaffari et al., 2021).

• Lines 814-819: Ultimately, the development of task-relevant scene-processing algorithms will likely benefit both from computational optimization experiments as well as exploratory SPV studies with human observers. With the presented simulator we aim to contribute a flexible toolkit for such experiments.

• Lines 842-853: Eventually, the functional quality of the artificial vision will not only depend on the correspondence between the visual environment and the phosphene encoding, but also on the implant recipient's ability to extract that information into a usable percept. The functional quality of end-to-end generated phosphene encodings in daily life tasks will need to be evaluated in future experiments. Regardless of the implementation, it will always be important to include human observers (both sighted experimental subjects and actual prosthetic implant users in the optimization cycle to ensure subjective interpretability for the end user (Fauvel et al., 2022; Beyeler & Sanchez-Garcia, 2022).

3) The results seem to assume that all phosphenes are small Gaussian blobs, and that these phosphenes combine linearly when multiple electrodes are stimulated. Both assumptions are frequently challenged by the field. For all these reasons, it is challenging to assess the potential and practical utility of this approach as well as get a sense of its limitations.

The reviewer raises a valid point and a similar point was raised by a different reviewer (our response is duplicated). As pointed out in the discussion, many aspects about multi- electrode phosphene perception are still unclear. On the one hand, the literature is in agreement that there is some degree of predictability: some papers explicitly state that phosphenes produced by multiple patterns are generally additive (Dobelle & Mladejovsky, 1974), that the locations are predictable (Bosking et al., 2018) and that multi-electrode stimulation can be used to generate complex, interpretable patterns of phosphenes (Chen et al., 2020, Fernandez et al., 2021). On the other hand, however, in some cases, the stimulation of multiple electrodes is reported to lead to brighter phosphenes (Fernandez et al., 2021), fused or displaced phosphenes (Schmidt et al., 1996, Bak et al., 1990) or unpredicted phosphene patterns (Fernández et al., 2021). It is likely that the probability of these interference patterns decreases when the distance between the stimulated electrodes increases. An empirical finding is that the critical distance for intracortical stimulation is approximately 1 mm (Ghose & Maunsell, 2012).

We note that our simulator is not restricted to the simulation of linearly combined Gaussian blobs. Some irregularities, such as elongated phosphene shapes were already supported in the previous version of our software. Furthermore, we added a supplementary figure that displays a possible approach to simulate some of the more complex electrode interactions that are reported in the literature, with only minor adaptations to the code. Our study thereby aims to present a flexible simulation toolkit that can be adapted to the needs of the user.

Adjustments:

• Added Figure 1-figure supplement 3 on irregular phosphene percepts.

• Lines 957-970: Furthermore, in contrast to the assumptions of our model, interactions between simultaneous stimulation of multiple electrodes can have an effect on the phosphene size and sometimes lead to unexpected percepts (Fernandez et al., 2021, Dobelle & Mladejovsky 1974, Bak et al., 1990). Although our software supports basic exploratory experimentation of non-linear interactions (see Figure 1-figure supplement 3), by default, our simulator assumes independence between electrodes. Multi- phosphene percepts are modeled using linear summation of the independent percepts. These assumptions seem to hold for intracortical electrodes separated by more than 1 mm (Ghose & Maunsell, 2012), but may underestimate the complexities observed when electrodes are nearer. Further clinical and theoretical modeling work could help to improve our understanding of these non-linear dynamics.

4) Another weakness of the paper is the term "biologically plausible", which appears throughout the manuscript but is not clearly defined. In its current form, it is not clear what makes this simulator "biologically plausible" - it certainly contains a retinotopic map and is fit on psychophysical data, but it does not seem to contain any other "biological" detail.

We thank the reviewer for the remark. We improved our description of what makes the simulator “biologically plausible” in the introduction (line 78): ‘‘Biological plausibility, in our work's context, points to the simulation's ability to capture essential biological features of the visual system in a manner consistent with empirical findings: our simulator integrates quantitative findings and models from the literature on cortical stimulation in V1 [...]”. In addition, we mention in the discussion (lines 611 - 621): “The aim of this study is to present a biologically plausible phosphene simulator, which takes realistic ranges of stimulation parameters, and generates a phenomenologically accurate representation of phosphene vision using differentiable functions. In order to achieve this, we have modeled and incorporated an extensive body of work regarding the psychophysics of phosphene perception. From the results presented in section H, we observe that our simulator is able to produce phosphene percepts that match the descriptions of phosphene vision that were gathered in basic and clinical visual neuroprosthetics studies over the past decades.”

5) In fact, for the most part the paper seems to ignore the fact that implanting a prosthesis in one cerebral hemisphere will produce phosphenes that are restricted to one half of the visual field. Yet Figures 6 and 8 present phosphenes that seemingly appear in both hemifields. I do not find this very "biologically plausible".

We agree with the reviewer that contemporary experiments with implantable electrodes usually test electrodes in a single hemisphere. However, future clinically useful approaches should use bilaterally implanted electrode arrays. Our simulator can either present phosphene locations in either one or both hemifields.

We have made the following textual changes:

• Fig. 1 caption: Example renderings after initializing the simulator with four 10 × 10 electrode arrays (indicated with roman numerals) placed in the right hemisphere (electrode spacing: 4 mm, in correspondence with the commonly used 'Utah array' (Maynard et al., 1997)).

• Line 518-525: The simulator is initialized with 1000 possible phosphenes in both hemifields, covering a field of view of 16 degrees of visual angle. Note that the simulated electrode density and placement differs from current prototype implants and the simulation can be considered to be an ambitious scenario from a surgical point of view, given the folding of the visual cortex and the part of the retinotopic map in V1 that is buried in the calcarine sulcus. Line 546-547: with the same phosphene coverage as the previously described experiment

Reviewer #2 (Public Review):

Van der Grinten and De Ruyter van Steveninck et al. present a design for simulating cortical- visual-prosthesis phosphenes that emphasizes features important for optimizing the use of such prostheses. The characteristics of simulated individual phosphenes were shown to agree well with data published from the use of cortical visual prostheses in humans. By ensuring that functions used to generate the simulations were differentiable, the authors permitted and demonstrated integration of the simulations into deep-learning algorithms. In concept, such algorithms could thereby identify parameters for translating images or videos into stimulation sequences that would be most effective for artificial vision. There are, however, limitations to the simulation that will limit its applicability to current prostheses.

The verification of how phosphenes are simulated for individual electrodes is very compelling. Visual-prosthesis simulations often do ignore the physiologic foundation underlying the generation of phosphenes. The authors' simulation takes into account how stimulation parameters contribute to phosphene appearance and show how that relationship can fit data from actual implanted volunteers. This provides an excellent foundation for determining optimal stimulation parameters with reasonable confidence in how parameter selections will affect individual-electrode phosphenes.

We thank the reviewer for these supportive comments.

Issues with the applicability and reliability of the simulation are detailed below:

1) The utility of this simulation design, as described, unfortunately breaks down beyond the scope of individual electrodes. To model the simultaneous activation of multiple electrodes, the authors' design linearly adds individual-electrode phosphenes together. This produces relatively clean collections of dots that one could think of as pixels in a crude digital display. Modeling phosphenes in such a way assumes that each electrode and the network it activates operate independently of other electrodes and their neuronal targets. Unfortunately, as the authors acknowledge and as noted in the studies they used to fit and verify individual-electrode phosphene characteristics, simultaneous stimulation of multiple electrodes often obscures features of individual-electrode phosphenes and can produce unexpected phosphene patterns. This simulation does not reflect these nonlinearities in how electrode activations combine. Nonlinearities in electrode combinations can be as subtle the phosphenes becoming brighter while still remaining distinct, or as problematic as generating only a single small phosphene that is indistinguishable from the activation of a subset of the electrodes activated, or that of a single electrode.

If a visual prosthesis happens to generate some phosphenes that can be elicited independently, a simulator of this type could perhaps be used by processing stimulation from independent groups of electrodes and adding their phosphenes together in the visual field.

The reviewer raises a valid point and a similar point was raised by a different reviewer (our response is duplicated). As pointed out in the discussion, many aspects about multi- electrode phosphene perception are still unclear. On the one hand, the literature is in agreement that there is some degree of predictability: some papers explicitly state that phosphenes produced by multiple patterns are generally additive (Dobelle & Mladejovsky, 1974), that the locations are predictable (Bosking et al., 2018) and that multi-electrode stimulation can be used to generate complex, interpretable patterns of phosphenes (Chen et al., 2020, Fernandez et al., 2021). On the other hand, however, in some cases, the stimulation of multiple electrodes is reported to lead to brighter phosphenes (Fernandez et al., 2021), fused or displaced phosphenes (Schmidt et al., 1996, Bak et al., 1990) or unpredicted phosphene patterns (Fernández et al., 2021). It is likely that the probability of these interference patterns decreases when the distance between the stimulated electrodes increases. An empirical finding is that the critical distance for intracortical stimulation is approximately 1 mm (Ghose & Maunsell, 2012).

We note that our simulator is not restricted to the simulation of linearly combined Gaussian blobs. Some irregularities, such as elongated phosphene shapes were already supported in the previous version of our software. Furthermore, we added a supplementary figure that displays a possible approach to simulate some of the more complex electrode interactions that are reported in the literature, with only minor adaptations to the code. Our study thereby aims to present a flexible simulation toolkit that can be adapted to the needs of the user.

Adjustments:

• Lines 957-970: Furthermore, in contrast to the assumptions of our model, interactions between simultaneous stimulation of multiple electrodes can have an effect on the phosphene size and sometimes lead to unexpected percepts (Fernandez et al., 2021, Dobelle & Mladejovsky 1974, Bak et al., 1990). Although our software supports basic exploratory experimentation of non-linear interactions (see Figure 1-figure supplement 3), by default, our simulator assumes independence between electrodes. Multi- phosphene percepts are modeled using linear summation of the independent percepts. These assumptions seem to hold for intracortical electrodes separated by more than 1 mm (Ghose & Maunsell, 2012), but may underestimate the complexities observed when electrodes are nearer. Further clinical and theoretical modeling work could help to improve our understanding of these non-linear dynamics.

• Added Figure 1-figure supplement 3 on irregular phosphene percepts.

2) Verification of how the simulation renders individual phosphenes based on stimulation parameters is an important step in confirming agreement between the simulation and the function of implanted devices. That verification was well demonstrated. The end use a visual-prosthesis simulation, however, would likely not be optimizing just the appearance of phosphenes, but predicting and optimizing functional performance in visual tasks. Investigating whether this simulator can suggest visual-task performance, either with sighted volunteers or a decoder model, that is similar to published task performance from visual-prosthesis implantees would be a necessary step for true validation.

We agree with the reviewer that it will be vital to investigate the utility of the simulator in tasks. However, the literature on the performance of users of a cortical prosthesis in visually-guided tasks is scarce, making it difficult to compare task performance between simulated versus real prosthetic vision.

Secondly, the main objective of the current study is to propose a simulator that emulates the sensory / perceptual experience, i.e. the low-level perceptual correspondence. Once more behavioral data from prosthetic users become available, studies can use the simulator to make these comparisons.

Regarding the comparison to simulated prosthetic vision in sighted volunteers, there are some fundamental limitations. For instance, sighted subjects are exposed for a shorter duration to the (simulated) artificial percept and lack the experience and training that prosthesis users get. Furthermore, sighted subjects may be unfamiliar with compensation strategies that blind individuals have developed. It will therefore be important to conduct clinical experiments.

To convey more clearly that our experiments are performed to verify the practical usability in future behavioral experiments, we have incorporated the following textual adjustments:

• Lines 275-279: In the sections below, we discuss the different components of the simulator model, followed by a description of some showcase experiments that assess the ability to fit recent clinical data and the practical usability of our simulator in simulation experiments.

• Lines 842-853: Eventually, the functional quality of the artificial vision will not only depend on the correspondence between the visual environment and the phosphene encoding, but also on the implant recipient's ability to extract that information into a usable percept. The functional quality of end-to-end generated phosphene encodings in daily life tasks will need to be evaluated in future experiments. Regardless of the implementation, it will always be important to include human observers (both sighted experimental subjects and actual prosthetic implant users in the optimization cycle to ensure subjective interpretability for the end (Fauvel et al., 2022; Beyeler & Sanchez- Garcia, 2022).

3) A feature of this simulation is being able to convert stimulation of V1 to phosphenes in the visual field. If used, this feature would likely only be able to simulate a subset of phosphenes generated by a prosthesis. Much of V1 is buried within the calcarine sulcus, and electrode placement within the calcarine sulcus is not currently feasible. As a result, stimulation of visual cortex typically involves combinations of the limited portions of V1 that lie outside the sulcus and higher visual areas, such as V2.

We agree that some areas (most notably the calcarine sulcus) are difficult to access in a surgical implantation procedure. A realistic simulation of state-of-the-art cortical stimulation should only partially cover the visual field with phosphenes. However, it may be predicted that some of these challenges will be addressed by new technologies. We chose to make the simulator as generally applicable as possible and users of the simulator can decide which phosphene locations are simulated. To demonstrate that our simulator can be flexibly initialized to simulate specific implantation locations using third- party software, we have now added a supplementary figure (Figure 1-figure supplement 1) that displays a demonstration of an electrode grid placement on a 3D brain model, generating the phosphene locations from receptive field maps. However, the simulator is general and can also be used to guide future strategies that aim to e.g. cover the entire field with electrodes, compare performance between upper and lower hemifields etc.

Reviewer #3 (Public Review):

The authors are presenting a new simulation for artificial vision that incorporates many recent advances in our understanding of the neural response to electrical stimulation, specifically within the field of visual prosthetics. The authors succeed in integrating multiple results from other researchers on aspects of V1 response to electrical stimulation to create a system that more accurately models V1 activation in a visual prosthesis than other simulators. The authors then attempt to demonstrate the value of such a system by adding a decoding stage and using machine-learning techniques to optimize the system to various configurations.

1) While there is merit to being able to apply various constraints (such as maximum current levels) and have the system attempt to find a solution that maximizes recoverable information, the interpretability of such encodings to a hypothetical recipient of such a system is not addressed. The authors demonstrate that they are able to recapitulate various standard encodings through this automated mechanism, but the advantages to using it as opposed to mechanisms that directly detect and encode, e.g., edges, are insufficiently justified.

We thank the reviewer for this constructive remark. Our simulator is designed for more realistic assessment of different stimulation protocols in behavioral experiments or in computational optimization experiments. The presented end-to-end experiments are a demonstration of the practical usability of our simulator in computational experiments, building on a previously existing line of research. In fact, our simulator is compatible with any arbitrary encoding strategy.

As our paper is focused on the development of a novel tool for this existing line of research, we do not aim to make claims about the functional quality of end-to-end encoders compared to alternative encoding methods (such as edge detection). That said, we agree with the reviewer that it is useful to discuss the benefits of end-to-end optimization compared to e.g. edge detection will be useful.

We have incorporated several textual changes to give a more nuanced overview and to acknowledge that many benefits remain to be tested. Furthermore, we have restated our study aims more clearly in the discussion to clarify the distinction between the goals of the current paper and the various encoding strategies that remain to be tested.

• Lines 275-279: In the sections below, we discuss the different components of the simulator model, followed by a description of some showcase experiments that assess the ability to fit recent clinical data and the practical usability of our simulator in simulation experiments

• Lines 810-814: Computational optimization approaches can also aid in the development of safe stimulation protocols, because they allow a faster exploration of the large parameter space and enable task-driven optimization of image processing strategies (Granley et al., 2022; Fauvel et al., 2022; White et al., 2019; Küçükoglü et al. 2022; de Ruyter van Steveninck, Güçlü et al., 2022; Ghaffari et al., 2021).

• Lines 842-853: Eventually, the functional quality of the artificial vision will not only depend on the correspondence between the visual environment and the phosphene encoding, but also on the implant recipient's ability to extract that information into a usable percept. The functional quality of end-to-end generated phosphene encodings in daily life tasks will need to be evaluated in future experiments. Regardless of the implementation, it will always be important to include human observers (both sighted experimental subjects and actual prosthetic implant users in the optimization cycle to ensure subjective interpretability for the end user (Fauvel et al., 2022; Beyeler & Sanchez-Garcia, 2022).

2) The authors make a few mistakes in their interpretation of biological mechanisms, and the introduction lacks appropriate depth of review of existing literature, giving the reader the mistaken impression that this is simulator is the only attempt ever made at biologically plausible simulation, rather than merely the most recent refinement that builds on decades of work across the field.

We thank the reviewer for this insight. We have improved the coverage of the previous literature to give credit where credit is due, and to address the long history of simulated phosphene vision.

Textual changes:

• Lines 64-70: Although the aforementioned SPV literature has provided us with major fundamental insights, the perceptual realism of electrically generated phosphenes and some aspects of the biological plausibility of the simulations can be further improved and by integrating existing knowledge of phosphene vision and its underlying physiology.

• Lines 164-190: The aforementioned studies used varying degrees of simplification of phosphene vision in their simulations. For instance, many included equally-sized phosphenes that were uniformly distributed over the visual field (informally referred to as the ‘scoreboard model’). Furthermore, most studies assumed either full control over phosphene brightness or used binary levels of brightness (e.g. 'on' / 'off'), but did not provide a description of the associated electrical stimulation parameters. Several studies have explicitly made steps towards more realistic phosphene simulations, by taking into account cortical magnification or using visuotopic maps (Fehervari et al., 2010;, Li et al., 2013; Srivastava et al., 2009; Paraskevoudi et al., 2021), simulating noise and electrode dropout (Dagnelie et al., 2007), or using varying levels of brightness (Vergnieux et al., 2017; Sanchez-Garcia et al., 2022; Parikh et al., 2013). However, no phosphene simulations have modeled temporal dynamics or provided a description of the parameters used for electrical stimulation. Some recent studies developed descriptive models of the phosphene size or brightness as a function of the stimulation parameters (Winawer et al., 2016; Bosking et al., 2017). Another very recent study has developed a deep-learning based model for predicting a realistic phosphene percept for single stimulating electrodes (Granley et al., 2022). These studies have made important contributions to improve our understanding of the effects of different stimulation parameters. The present work builds on these previous insights to provide a full simulation model that can be used for the functional evaluation of cortical visual prosthetic systems.

• Lines 137-140: Due to the cortical magnification (the foveal information is represented by a relatively large surface area in the visual cortex as a result of variation of retinal RF size) the size of the phosphene increases with its eccentricity (Winawer & Parvizi, 2016, Bosking et al., 2017).

• Lines 883-893: Even after loss of vision, the brain integrates eye movements for the localization of visual stimuli (Reuschel et al., 2012), and in cortical prostheses the position of the artificially induced percept will shift along with eye movements (Brindley & Lewin, 1968, Schmidt et al., 1996). Therefore, in prostheses with a head-mounted camera, misalignment between the camera orientation and the pupillary axes can induce localization problems (Caspi et al., 2018; Paraskevoudi & Pezaris, 2019; Sabbah et al., 2014; Schmidt et al., 1996). Previous SPV studies have demonstrated that eye-tracking can be implemented to simulate the gaze-coupled perception of phosphenes (Cha et al., 1992; Sommerhalder et al., 2004; Dagnelie et al., 2006; McIntosh et al., 2013, Paraskevoudi & Pezaris, 2021; Rassia & Pezaris 2018, Titchener et al., 2018, Srivastava et al., 2009)

3) The authors have importantly not included gaze position compensation which adds more complexity than the authors suggest it would, and also means the simulator lacks a basic, fundamental feature that strongly limits its utility.

We agree with the reviewer that the inclusion of gaze position to simulate gaze-centered phosphene locations is an important requirement for a realistic simulation. We have made several textual adjustments to section M1 to improve the clarity of the explanation and we have added several references to address the simulation literature that took eye movements into account.

In addition, we included a link to some demonstration videos in which we illustrate that the simulator can be used for gaze-centered phosphene simulation. The simulation models the phosphene locations based on the gaze direction, and updates the input with changes in the gaze direction. The stimulation pattern is chosen to encode the visual environment at the location where the gaze is directed. Gaze contingent processing has been implemented in prior simulation studies (for instance: Paraskevoudi et al., 2021; Rassia et al., 2018; Titchener et al., 2018) and even in the clinical setting with users of the Argus II implant (Caspi et al., 2018). From a modeling perspective, it is relatively straightforward to simulate gaze-centered phosphene locations and gaze contingent image processing (our code will be made publicly available). At the same time, however, seen from a clinical and hardware engineering perspective, the implementation of eye-tracking in a prosthetic system for blind individuals might come with additional complexities. This is now acknowledged explicitly in the manuscript.

Textual adjustment:

Lines 883-910: Even after loss of vision, the brain integrates eye movements for the localization of visual stimuli (Reuschel et al., 2012), and in cortical prostheses the position of the artificially induced percept will shift along with eye movements (Brindley & Lewin, 1968, Schmidt et al., 1996). Therefore, in prostheses with a head-mounted camera, misalignment between the camera orientation and the pupillary axes can induce localization problems (Caspi et al., 2018; Paraskevoudi & Pezaris, 2019; Sabbah et al., 2014; Schmidt et al., 1996). Previous SPV studies have demonstrated that eye-tracking can be implemented to simulate the gaze-coupled perception of phosphenes (Cha et al., 1992; Sommerhalder et al., 2004; Dagnelie et al., 2006, McIntosh et al., 2013; Paraskevoudi et al., 2021; Rassia et al., 2018; Titchener et al., 2018; Srivastava et al., 2009). Note that some of the cited studies implemented a simulation condition where not only the simulated phosphene locations, but also the stimulation protocol depended on the gaze direction. More specifically, instead of representing the head-centered camera input, the stimulation pattern was chosen to encode the external environment at the location where the gaze was directed. While further research is required, there is some preliminary evidence that such a gaze-contingent image processing can improve the functional and subjective quality of prosthetic vision (Caspi et al., 2018; Paraskevoudi et al., 2021; Rassia et al., 2018; Titchener et al., 2018). Some example videos of gaze-contingent simulated prosthetic vision can be retrieved from our repository (https://github.com/neuralcodinglab/dynaphos/blob/main/examples/). Note that an eye-tracker will be required to produce gaze-contingent image processing in visual prostheses and there might be unforeseen complexities in the clinical implementation thereof. The study of oculomotor behavior in blind individuals (with or without a visual prosthesis) is still an ongoing line of research (Caspi et al.,2018; Kwon et al., 2013; Sabbah et al., 2014; Hafed et al., 2016).

4) Finally, the computational capacity required to run the described system is substantial and is not one that would plausibly be used as part of an actual device, suggesting that there may be difficulties with converting results from this simulator to an implantable system.

The software runs in real time with affordable, consumer-grade hardware. In Author response image 1 we present the results of performance testing with a 2016 model MSI GeForce GTX 1080 (priced around €600).

Author response image 1.

Note that the GPU is used only for the computation and rendering of the phosphene representations from given electrode stimulation patterns, which will never be part of any prosthetic device. The choice of encoder to generate the stimulation patterns will determine the required processing capacity that needs to be included in the prosthetic system, which is unrelated to the simulator’s requirements.

The following addition was made to the text:

• Lines 488-492: Notably, even on a consumer-grade GPU (e.g. a 2016 model GeForce GTX 1080) the simulator still reaches real-time processing speeds (>100 fps) for simulations with 1000 phosphenes at 256x256 resolution.

5) With all of that said, the results do represent an advance, and one that could have wider impact if the authors were to reduce the computational requirements, and add gaze correction.

We appreciate the kind compliment from the reviewer and sincerely hope that our revised manuscript meets their expectations. Their feedback has been critical to reshape and improve this work.

Author Response

Reviewer #3 (Public Review):

In this manuscript, the authors studied the erythropoiesis and hematopoietic stem/progenitor cell (HSPC) phenotypes in a ribosome gene Rps12 mutant mouse model. They found that RpS12 is required for both steady and stress hematopoiesis. Mechanistically, RpS12+/- HSCs/MPPs exhibited increased cycling, loss of quiescence, protein translation rate, and apoptosis rates, which may be attributed to ERK and Akt/mTOR hyperactivation. Overall, this is a new mouse model that sheds light into our understanding of Rps gene function in murine hematopoiesis. The phenotypic and functional analysis of the mice are largely properly controlled, robust, and analyzed.

A major weakness of this work is its descriptive nature, without a clear mechanism that explains the phenotypes observed in RpS12+/- mice. It is possible that the counterintuitive activation of ERK/mTOR pathway and increased protein synthesis rate is a compensatory negative feedback. Direct mechanism of Rps12 loss could be studied by ths acute loss of Rps12, which is doable using their floxed mice. At the minimum, this can be done in mammalian hematopoietic cell lines.

We thank the reviewer for pointing this out. We have addressed this question by developing a new inducible conditional knockout Rps12 mouse model (see response below to major point 1).

Below are some specific concerns need to be addressed.

1) Line 226. The authors conclude that "Together, these results suggest that RpS12 plays an essential role in HSC function, including self-renewal and differentiation." The reviewer has three concerns regarding this conclusion and corresponding Figure3. 1) The data shows that RpS12+/- mice have decreased number of both total BM cells and multiple subpopulations of HSPCs. The frequency of HSPC subpopulations should also be shown to clarify if the decreased HSPC numbers arises from decreased total BM cellularity or proportionally decrease in frequency. 2) This figure characterizes phenotypic HSPC in BM by flow and lineage cells in PB by CBC. HSC function and differentiation are not really examined in this figure, except for the colony assay in Figure 3K. BMT data in Figure4 is actually for HSC function and differentiation. So the conclusion here should be rephrased. 3) Since all LT-, ST-HSCs, as well as all MPPs are decreased in number, how can the authors conclude that Rps12 is important for HSC differentiation? No experiments presented here were specifically designed to address HSC differentiation.

We thank the reviewer for this excellent point. We think that the main defect is in HSC and progenitor maintenance, rather than in HSC differentiation. This is consistent with the decrease in multiple HSC and progenitor populations, as observed both by calculating absolute numbers and by frequency of the parent population (see new Supplementary Figures S2C-S2C). We have removed any references to altered differentiation from the text.

We added data on the population frequency in the Supplementary Figure 2. And in the corresponding text. See lines 221-235.

2) Figure 3A and 5E. The flow cytometry gating of HSC/MPP is not well performed or presented, especially HSC plot. Populations are not well separated by phenotypic markers. This concerns the validity of the quantification data.

We chose a better representative HSC plot and included it in the Figure 3A

3) It is very difficult to read bone marrow cytospin images in Fig 6F without annotation of cell types shown in the figure. It appears that WT and +/- looked remarkably different in terms of cell size and cell types. This mouse may have other profound phenotypes that need detailed examination, such as lineage cells in the BM and spleen, and colony assays for different types of progenitors, etc.

The purpose of the bone marrow cytospin images in Figure 6F was to show the high number of apoptotic cells in the bone marrow of Rps12 KO/+ mice compared with controls. The differences in apoptosis in the LSK and myeloid progenitor populations are quantified in the flow cytometry data shown in Figure 6G-H. A detailed quantitative analysis of different bone marrow cell populations and their relative frequencies is also shown in Figures 2 and 3. In Rps12 KO/+ bone marrow, we observed a significant decrease in multiple stem cell and progenitor populations.

4) For all the intracellular phospho-flow shown in Fig7, both a negative control of a fluorescent 2nd antibody only and a positive stimulus should be included. It is very concerning that no significant changes of pAKT and pERK signaling (MFI) after SCF stimulation from the histogram in WT LSKs. There are no distinct peaks that indicate non-phospho-proteins and phosphoproteins. This casts doubt on the validity of results. It is possible though that Rsp12+/- have very high basal level of activation of pAKT/mTOR and pERK pathway. This again may point to a negative feedback mechanism of Rps12 haploinsufficiency.

It is true that we did not observe an increase in pAKT, p4EBP1, or pERK in control cells in every case. This is often an issue with these specific phospho-flow cytometry antibodies, as they are not very sensitive, and the response to SCF is very time-dependent. We did observe an increase in pS6 with SCF in both LSK cells and progenitors (Figure 7B, E). However, the main point of this experiment was to assess the basal level of signaling in Rps12 KO/+ vs control cells. We did not observe hypersensitivity of RpS12 cells to SCF, but we did observe significant increases in pAKT, pS6, p4EBP1, and pERK in Rsp12 KO/+ LSK cells.

To address the concern about the validity of staining, please see the requested flow histograms for unstained vs individual Phospho-antibodies (Ab): p4EBP1, pERK, pS6 and pAKT (Figure R1 for reviewers) below. Additionally, since staining with the surface antibodies potentially can change the peak, we are including additional an control of the cell surface antibodies vs full sample with surface antibodies and Phospho-Ab: p4EBP1, pERK, pS6 and pAKT. We can include this figure in the Supplementary Data if requested.

5) The authors performed in vitro OP-Puro assay to assess the global protein translation in different HSPC subpopulations. 1) Can the authors provide more information about the incubation media, any cytokine or serum included? The incubation media with supplements may boost the overall translation status, although cells from WT and RpS12+/- are cultured side by side. Based on this, in vivo OP-Puro assay should be performed in both genotypes. 2) Polysome profiling assay should be performed in primary HSPCs, or at least in hematopoietic cell lines. It is plausible that RpS12 haploinsufficiency may affect the content of translational polysome fractions.

We are including these details in the methods section: for in vitro OP-Puro assay (lines 555565) cells were resuspended in DMEM (Corning 10-013-CV) media supplemented with 50 µM β-mercaptoethanol (Sigma) and 20 µM OPP (Thermo Scientific C10456). Cells were incubated for 45 minutes at 37°C and then washed with Ca2+ and Mg2+ free PBS. No additional cytokines were added.

We did not perform polysome profiles. Polysome profiling of mutant stem and progenitor cells would be very challenging, as their numbers are much reduced. We now deem this of reduced interest, given the conclusion of the revised manuscript that RpS12 haploinsufficiency reduces overall translation. Also, because in RpS12-floxed/+;SCL-CRE-ERT mouse model with acute deletion of RpS12 we observed the expected decrease in translation in HSCs using the same ex vivo OPP protocol, we did not follow up with in vivo OPP treatment,

Author Response

Reviewer #1 (Public Review):

The authors have used many cleverly chosen mouse models (periodontitis models; various models that lead to an on-switch of genes) and methods (immune localizations of high quality; single cell RNA sequencing) for the quest of elucidating a role for telocytes. They describe that more telocytes are present around teeth in mice that had periodontitis. These cells proliferated, and they expressed a pattern of genes that allowed macrophages to differentiate into a different direction. In particular, they showed that telocytes in periodontitis express HGF, a molecule that steers macrophage differentiation towards a less inflammatory cell type, paving the way for recovery. As a weakness, one could state that an attempt to extrapolate to human cells is missing.

In the Discussion, we have a sentence that states further investigation in human periodontitis is required (see page 20, paragraph 416).

Reviewer #3 (Public Review):

Zhao and Sharpe identified telocytes in the periodontium. To address their contribution to periodontal diseases, they conducted scRNA-seq analysis and lineage tracing in mice. They demonstrated that telocytes are activated in periodontitis. The activated telocytes send HGF signals to surrounding macrophages, converting M2 to M1/M2 hybrid status. The study implies that targeting telocytes and HGF signal for the potential treatment of periodontitis.

The significance of the study could be improved by authors testing if targeting telocytes or HGF signals could ameliorate periodontitis in the mouse model. The current form of the manuscript lacks the data that demonstrate the actual contribution of telocytes in the homeostasis of periodontium or progression of periodontitis.

Major comments:

1) I see the genetic validation of the role of telocytes or HGF signals are crucial to assure the significance of this manuscript. I recommend either of two experiments. a. testing the role of HGF signals by deleting the Hgf gene in telocytes. Using Wnt11-Cre; Hgf f/f mice, the authors could address the role of HGF signals in periodontitis. CX3CR1-Cre; cMet f/f mice will delete HGF signals in monocyte-derived macrophages. This will be another verification, but not sure if the PDL macrophages are derived from yolk sac or monocytes. b. measuring the contribution of telocytes in the homeostasis or disease progression. The mouse model could be challenging though, the system if achieved will be very informative. The authors could first check the expression of telocyte enriched genes, such as Lgr5 or Foxl1 reported previously in other tissue telocytes. Delete those genes under the Wnt1-Cre driver and check if telocyte lineage is removed. The system would be very useful for next-level study. DTA model could be an alternative, but Wnt1-Cre is vastly expressed in neural crest lineage.

These are good suggestions but unfortunately not feasible as we do not have all the mouse lines (e.g., Hgf f/f mice). Lgr5 and Foxl1 are used in intestine but is not suitable for PDL tissue. CD34;DTA show CD34+ cells, however, we encountered challenges associated with induced genetic heterogeneity when using this model, preventing us from making concrete conclusions from the experiments using the CD34;DTA model. Lgf5/Foxl1 are either not expressed or overlap with CD34 in and therefore do not seem suitable for us to pursue.

2) This paper points out that the M1/M2 hybrid state of macrophages appears upon periodontitis. The authors could further characterize the hybrid macrophages by the expression of more markers, production of cytokines, and morphology. Need to clarify if this means some macrophages are in M1 state and others are in M2 state, or one macrophage possesses both M1 and M2 phenotype. Please conduct either FACS or immunofluorescence to demonstrate if one macrophage expresses both markers. Please introduce more information about the M1/M2 hybrid state of macrophage based on other present literature.

Unlike our single cell sequencing data, we were unsuccessful in determining if one macrophage possesses both M1 and M2 phenotype by immunolabelling.

3) In the introduction part, the author lists several markers that can be used for telocyte identification, such as CD34+CD31-, CD34+c-Kit+, CD34+Vim+, CD34+PDGFRα+. Could authors explain why they chose CD34 CD31, but not other markers?

As shown in the cluster images below, the other markers do not overlap very well with CD34 cells or in the case of Vim, expressed more ubiquitously. We generated a new supplementary figure (Supp Fig2) and explained this in the text (page 12, lines 235-238).

4) In figure 5g, I don't think the yellow color cell shows the reduction trend in the Tivantinib treatment group compared with a control group. Please validate the observation by gene expression analysis, WB, etc. In addition, please show c-Met+ cells level in the Tivantinib treatment group and control group.

New Supp Fig4 is included to show Met expression in homeostasis and periodontitis.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Li et al characterize sex differences in the impact of macrophage RELMa in protection against diet-induced obesity [DIO]. This is a key area of interest as obesity studies in mice have generally focused exclusively on male animals, as they tend to gain more weight, faster than female mice. The authors use a combination of flow cytometry, adoptive transfer, and single-cell transcriptomics to characterize the mechanism of action for female-specific DIO protection. They identify a potential role for eosinophils in mediating female DIO protection downstream of RELMa production by macrophage. They also use the transcriptomic characterization of the stromal vascular fraction of the adipose tissue to evaluate molecular and cellular drivers of this sex-specific DIO protection.

Although the authors provide solid evidence for many claims in the manuscript, there is generally not enough information about the studies' methods (especially on the computational/data analysis aspects) for a careful evaluation of the result's robustness at this stage.

We have significantly expanded the methodology, especially of the scRNAseq, and deposited the script and raw data in public repositories. We also validated our methods and can confirm that the analysis presented is robust. This resubmission contains new Fig 7 and new supplementary material with this methodology and validation.

Reviewer #2 (Public Review):

In the study by Li et al., the authors hypothesize that RELMa, a macrophage-derived protein, plays a sex-dimorphic role as a protective factor in obesity in females vs males. The authors perform largely in vivo studies utilizing male and female WT and RELMa KO mice on a high-fat diet and perform an in-depth analysis of immune cell composition, gene expression, and single-cell RNA Sequencing. The authors find that WT females are protected from obesity and inflammation vs males, and this protection is lost in female RELMa KO mice. Further analysis by the authors including flow cytometry of the visceral fat SVF in female WT mice showed reduced macrophage infiltration, higher levels of eosinophils, and Th2 cytokine expression compared to WT male mice and female KO mice. The authors show that protection from obesity and inflammation in female RELMa KO mice can be rescued with an injection of eosinophils and recombinant RELMa. Lastly, the authors use single-cell RNA-Sequencing to further analyze SVF cells in WT and KO male and female mice on a high-fat diet.

Overall, we find that the study represents an important finding in the immunometabolism field showing that RELMa is a key myeloid-derived factor that helps influence the macrophage-eosinophil function in female mice and protects from diet-induced obesity and inflammation in a sexually dimorphic manner. Overall, the study provides strong and convincing data supporting the authors' hypothesis and conclusion.

We thank the reviewer for their positive review of our manuscript and their helpful feedback which we address below.

Reviewer #3 (Public Review):

Li, Ruggiero-Ruff et al. examine the role of RELMα, an anti-inflammatory macrophage signature gene, in mediating sex differences in high-fat diet (HFD)-induced obesity in young mice. Specifically, the authors hypothesize that RELMα protects females against HFD-induced obesity. Comparisons between RELMα-knockout (KO) and wildtype (WT) mice of both sexes revealed sex- and RELMα-specific differences in weight gain, immune cell populations, and inflammatory signaling in response to HFD. RELMα-deficiency in females led to increased weight gain, expansion of pro-inflammatory macrophage populations, and eosinophil loss in response to HFD. Female RELMα-deficiency could be rescued by RELMα treatment or eosinophil transfer. Single-cell RNA-sequencing (scRNA-seq) of adipose stromal vascular fraction (SVF) revealed sex- and RELMα-dependent differences under HFD conditions and identified potential "pro-obesity" and "anti-obesity" genes in a cell-type-specific manner. Using trajectory analysis, the authors suggest dysregulation of macrophage-to-monocyte transition in RELMα-deficient mice.

The conclusions of this paper are mostly well supported by the data, but some aspects of the statistical and single-cell analyses will need to be corrected, clarified, and extended to enhance the report.

We thank Dr. Ocanas for their positive comments and for the helpful feedback to improve our study. We have addressed all the comments and significantly revised the manuscript.

Strengths:

The authors use several orthogonal approaches (i.e., flow cytometry, immunohistochemistry, scRNA-Seq) and models to support their hypotheses.

The authors demonstrate that phenotypes observed in HFD-fed females with RELMα-deficiency (i.e., weight gain, loss of eosinophils, a gain of M1 macrophages) can be rescued by RELMα treatment or eosinophil transfer.

The authors recognized the complexity of macrophage activation that is beyond the 'M1/M2' paradigm and informed readers in the introduction as to why this paradigm was used in this study. During the scRNA-seq analyses, the authors further sub-cluster macrophages to include more granularity.

Weaknesses:

1) There are several instances in the text where the authors claim that there is a significant difference between the two groups, but the statistics for these comparisons are not shown in the figure.

Because we are dealing with three variables: genotype, diet and sex, and many differences, we thought it too complicated to add all the significant differences on the graph, but sometimes just mentioned these in the text with a p value, or didn’t mention at all if the difference was obvious, or not meaningful (for example, we weren’t interested in comparing a WT male on a Ctr diet with a RELMalpha KO female on a HFD for the purpose of our hypothesis). We have now ensured clarity in the text and in the figures, and addressed the specific point-by-point comments from the reviewer. We have also now carefully re-evaluated the text to ensure that any significant differences we discuss are shown in the figure.

2) It is unfortunate that eosinophils could not be identified in the single-cell analysis since this population of cells was shown to be important in rescuing the RELMα-deficiency in HFD-fed females. The authors should note in the discussion how future scRNA-Seq experiments could overcome this limitation (i.e., enriching immune cells prior to scRNA-Seq).

We were indeed disappointed that we were not able to obtain eosinophil single cell seq, but realize that this is a reported issue in the field. We have expanded our discussion of this and cited a paper that performs eosinophil single cell sequencing (published at the time our manuscript was being submitted): ““At the same time as our ongoing analysis, the first publication of eosinophil single cell RNA-seq was published, using a flow cytometry based approach rather than 10x, including RNAse inhibitor in the sorting buffer, and performing prior eosinophil enrichment (PMID: 36509106). Based on guidance from 10x, we employed targeted approaches to identify eosinophil clusters according to eosinophil markers (e.g. Siglecf, Prg2, Ccr3, Il5r), and relaxed the scRNA-Seq cutoff analysis to include more cells and intronic content, but still could not find eosinophils. We conclude that eosinophils may be absent due to the enzyme digestion required for SVF isolation and processing for single cell sequencing, which could lead to specific eosinophil population loss due to low RNA content, RNases or cell viability issues. Future experiments would be needed to optimize eosinophil single cell sequencing, based on the recent publication of eosinophil single cell sequencing.”

3a) There are several issues with the scRNA-Seq analysis and interpretation. More details on the steps taken in the single-cell analyses should be included in the methods section.

We agree with the reviewer that more details on steps taken in the single cell data processing and bioinformatics needs to be included in the methods section. We included more information and separated sections within the data processing section in the Materials and Methods on the methodology used for these approaches, as well as provided a code for our data processing in a public Github repository: https://github.com/rrugg002/Sexual-dimorphism-in-obesity-is-governed-by-RELM-regulation-of-adipose-macrophages-and-eosinophils.

b) With regards to the 'pseudobulk' analyses presented in Figs. 5-6, several of the differentially expressed genes identified in Fig. 6 are hemoglobin genes (i.e., Hba, Hbb genes). It is not uncommon to filter these genes out of single-cell analysis since their presence usually indicates red blood cell (RBC) contamination (PMID: 31942070, PMID: 35672358). We would recommend assessing RBC contamination as well as removing Fig. 6 from the manuscript and focusing on cell-type-specific analyses. Re-analysis will likely have an impact on the overall conclusions of the study.

Prior to our first submission, we consulted with 10x support scientists and the UCR bioinformatics core director to ensure that our analysis included the appropriate filtering. We have now added details in the Methods. The PMIDs provided above are from studies that looked at hippocampus development (where they didn’t perfuse so there may be blood contamination) or whole blood (where there would be significant red blood cell contamination). In contrast, we perfused our mice and treated the single cell suspension with RBC lysis buffer, as detailed in Methods. Also, we have now extended our scSeq analysis to compare hemoglobin RNA to red blood cell specific markers including Gypa/CD235a. While hemoglobin is distributed throughout the myeloid population in the female KO mice, Gypa/CD235a, which would suggest RBC contamination is not expressed at all (see new Fig 7B). Additionally, we provide hemoglobin protein ELISA and IF staining to support our finding that macrophages from KO mice express hemoglobin protein. Last, two publications support hemoglobin expression by nonerythroid sources, including macrophages (PMID: 10359765; PMID: 25431740). While we are confident based on above that our data is not due to RBC contamination, we cannot exclude the fact that, although unlikely, macrophages may be phagocytosing RBC and preserving specifically hemoglobin RNA and protein. Nonetheless, we discuss this possibility in the text. In conclusion, based on the justification above and the new data, we are confident that our findings and overall conclusions are robust.

To assess for potential RBC contamination, in addition to Gypa, we additionally looked at top genes expressed by murine erythrocytes (PMID: 24637361). Please see below feature plots, showing little to no expression, and a very different distribution than the hemoglobin genes (see new Fig 7a):

Also, we had a small cluster of potential RBCs (only 75 cells) that we filtered out of downstream DEG analysis, which revealed the same data as in the first submission.

4) Within the text, there are several instances where the authors claim that a pathway is upregulated based on their Gene Ontology (GO) over-representation analysis (ORA). To come to this conclusion, the authors identify genes that are upregulated in one condition and then perform GO-ORA on these genes. However, the authors do not consider negative regulators, whose upregulation would actually decrease the pathway. Authors should either replace their GO-ORA analysis with one that considers the magnitude and direction of differentially expressed genes and provides an activation z-score (i.e., Ingenuity Pathway Analysis) or replace instances of 'upregulated' or 'downregulated' pathways with 'over-represented' pathways.

Unfortunately, we did not have access to IPA for this project, therefore we have changed our analysis to over and under-represented pathways as suggested.

5) For Fig.7A, a representative tSNE plot for each group (WT Female, KO Female, WT Male, KO Male) should be shown to ensure there is proper integration of the clusters across groups. There are some instances where the scRNA-Seq data do not appear to be integrated properly (i.e., Supplemental Figure 2C). The authors should explore integration techniques (i.e., Seurat; PMID: 29608179) to correct for potential batch effects within the analysis.

We thank the reviewer for the suggestion of proper integration of the clusters across groups. We performed integration using the Cell Ranger aggregation (aggr) pipeline (see updated materials and methods section). In addition, many technical controls were performed to prevent batch effects between our samples. For sequencing, we used the 10x genomics library sequencing depth and run parameters for both gene expression and multiplexing libraries. For all 3’ gene expression library sequencing, we sequenced at a depth of 20,000 read pairs per cell and for all cell multiplexing library sequencing we sequenced at a depth of 5,000 read pairs per cell. All libraries were paired-end dual indexed libraries and were pooled on one flow cell lane using a 4:1 ratio (3’ Gene expression: Multiplexing ratio) in the Novaseq, as recommended by 10x Genomics, in order to maintain nucleotide diversity and prevent batch effects during the sequencing process. When performing integration/aggregation of all sample gene expression libraries using the Cell Ranger aggregation (aggr) pipeline, we performed sequencing depth normalization between all samples. Cell Ranger does this by equalizing the average read depth per cell between groups before merging all sample libraries and counts together. This is a default setting in the Cell Ranger aggr pipeline, and this approach avoids artifacts that may be introduced due to differences in sequencing depth. Thus, we are confident that changes we observed in gene expression and cell type populations are due to biological differences and not technical variability. Below we have provided a tSNE plot showing clustering of all 12 samples after we performed integration:

We updated old Fig.7 (now Fig. 6) and included a representative tSNE plot for each group. We also updated the tSNE plot for Figure 5-figure supplement 2C (previously S2C) showing overall clustering amongst all groups. The largest population differences occurred in the fibroblast population and these population differences were largely due to sex differences. Because we are confident that integration was performed appropriately and that batch effects were controlled for, we believe these sex differences are a biological effect.

6) LncRNA Gm47283 is identified as a gene that is differentially expressed by genotype in HFD females (Fig. 7G); however, according to Ensembl this gene is encoded on the Y-chromosome (https://uswest.ensembl.org/Mus_musculus/Gene/Summary?g=ENSMUSG00000096768;r=Y:90796007-90827734). The authors should use the RELMα genotype and sex chromosomally-encoded genes to confirm that their multiplexing was appropriate.

We agree with the reviewer that it is crucial to confirm that multiplexing and all subsequent analyses are performed correctly. Comparison between males and females contains internal controls that increase confidence, such as Xist gene that is expressed only in females, and Ddx3y that is located on the Y chromosome. LncRNA, Gm47283 is located in the syntenic region of Y chromosome and is also present in females, annotated as Gm21887 located in the syntenic region of the X chromosome. It also has 100% alignment with Gm55594 on X chromosome. Additionally, it is also referred to erythroid differentiation regulator 1 (Erd1), x or y depending on the chromosome, although NCBI database specifies partial assembly and incomplete annotation. Therefore, this explains why we see expression of this gene in females. We have discussed this in the text. We revised the text to refer to this LncRNA as Gm47283/Gm21887 to prevent further confusion. The RELMalpha genotype (absence in the KO) was also confirmed. Last, the PC analysis (see Fig 5) supports clustering by group.

7) For Fig. 8, samples should be co-clustered and integrated across groups before performing trajectory analysis to allow for direct comparisons between groups.

We appreciate the valuable feedback and suggestions, which have been helpful in clarifying the trajectory analysis, which we have done as follows:

Regarding the co-clustering and integration of our samples across groups, here is the explanation of our trajectory analysis approach. We have co-clustered all of our samples using the align_cds function from the Monocle3 package. We have included the code for Figure 8 in our Github repository at https://github.com/rrugg002/Sexual-dimorphism-in-obesity-is-governed-by-RELM-regulation-of-adipose-macrophages-and-eosinophils/blob/main/Figure8.R. Specifically, lines 138, 166, 196 and 225 of the code indicate that the align_cds function was used to cluster our samples by "Sample.ID".

The align_cds function in Monocle3 can be used to co-cluster all samples in a single-cell RNA-seq experiment by aligning coding sequences (CDS) across different cell types or conditions. The align_cds function takes a set of reference CDS sequences and single-cell RNA-seq reads and identifies the CDS sequences within each read, allowing the identification of differentially expressed genes across different cell types or conditions based on the aligned CDS sequences. More details about align_cds can be found here https://rdrr.io/github/cole-trapnell-lab/monocle3/man/align_cds.html .

We hope that this additional information alleviates the reviewer’s concerns.

8) Since the experiments presented in this report were from young mice using a single diet intervention, the authors should comment on how age and other obesogenic diets may impact the results found here. Also, the authors should expand their discussion as to what upstream regulators (i.e., hormones or genetics) may be driving the sex differences in RELMα expression in response to HFD.

We thank the reviewer for the suggestion. We included several sentences to address this comment. However, since reviewers commented that some of the text needs to be trimmed down, extensive discussion regarding reasons for sex differences, which are numerous, are outside the scope of this manuscript. For example, sex differences can arise from all or any of these:

1. Sex steroid hormones (estrogen and testosterone) are an obvious possibility for sex differences and this discussion has been included below and in the text.

2. Sex differences we observe may stem from variety of other factors, besides ovarian estrogen; including extraovarian estrogen, primarily estrogen produced in adipose tissues (32119876).

3. Sex differences exist in fat deposition, which may or may not be estrogen dependent (25578600, 21834845).

4. Sex difference were determined in metabolic rate and oxidative phosphorylation, which may also be independent of estrogen (28650095, and reviewed in 26339468).

5. Sex differences exist in the immune system, some of which are estrogen independent, but dependent on sex chromosomes (32193609).

6. Sex differences particularly in myeloid lineage, which may also be estrogen independent (25869128).

7. Sex differences were determined in adipokine levels, including leptin and adiponectin, which influence immune cells in adipose tissues (33268480).

The role of estrogen is not clear either, and thus extensive discussion is not possible. Numerous studies demonstrated that estrogen is protective from inflammation, thus it is possible that estrogen drives some of the sex differences observed herein. However, several studies determined that estrogen can be pro-inflammatory (20554954, 15879140, 18523261). Previous publications by us (30254630, 33268480) and others (25869128) demonstrated intrinsic sex differences in immune system, that are maybe dependent on sex chromosome complement and/or Xist expression (34103397, 30671059).

Studies are more consistent that estrogen is protective from weight gain: postmenopausal women with diminished estrogen, and ovariectomized animal models gain weight. The effects of ovariectomy on weight gain and its additive effects with high fat diet were reported in Rhesus monkeys (for example PMID: 2663699; and PMID: 16421340); and in rodents (PMID: 7349433).

The reviewer is correct that the effects of aging or estrogen on RELMa levels would be of significant interest, and could be a future direction of our studies. Aging-mediated increase in inflammation (including of adipose tissue, recently reviewed in 36875140), that may be dependent on estrogen, can exacerbate obesity-mediated inflammation. We have added this discussion.

For these reasons we limited our discussion regarding possible differences and stated this in the discussion: “Several studies demonstrated the protective role of estrogen in obesity-mediated inflammation and in weight gain, as discussed above. Whether estrogen protection occurs via estrogen regulation of RELMa levels is a focus of our future studies. Alternatively, intrinsic sex differences in immune system have been demonstrated as well (30254630, 33268480, 25869128) that are dependent on sex chromosome complement and/or Xist expression (34103397, 30671059), and RELMa may be regulated by these as well. Additionally, ageing-mediated increase in inflammation (including of adipose tissue, recently reviewed in 36875140), may also occur via changes in RELMa levels. Our studies used young but developmentally mature mice (4-6 weeks old when placed on diet, 18 weeks old at sacrifice), and future work on aged mice would be needed to investigate aging-mediated inflammation. Furthermore, there are sex differences in fat deposition, metabolic rates and oxidative phosphorylation (reviewed in 26339468), and adipokine expression (Coss) that regulate cytokine and chemokines levels, and therefore may regulate levels of RELMa as well. These possibilities will be addressed in future studies.”

Author Response

Reviewer #1 (Public Review):

In this manuscript, Goering et al. investigate subcellular RNA localization across different cell types focusing on epithelial cells (mouse C2bbe1 and human HCA-7 enterocyte monolayers, canine MDCK epithelial cells) as well as neuronal cultures (mouse CAD cells). They use their recently established Halo-seq method to investigate transcriptome-wide RNA localization biases in C2bbe1 enterocyte monolayers and find that 5'TOP-motif containing mRNAs, which encode ribosomal proteins (RPs), are enriched on the basal side of these cells. These results are supported by smFISH against endogenous RP-encoding mRNAs (RPL7 and RPS28) as well as Firefly luciferase reporter transcripts with and without mutated 5'TOP sequences. Furthermore, they find that 5'TOP-motifs are not only driving localization to the basal side of epithelial cells but also to neuronal processes. To investigate the molecular mechanism behind the observed RNA localization biases, they reduce expression of several Larp proteins and find that RNA localization is consistently Larp1-dependent. Additionally, the localization depends on the placement of the TOP sequence in the 5'UTR and not the 3'UTR. To confirm that similar RNA localization biases can be conserved across cell types for other classes of transcripts, they perform similar experiments with a GA-rich element containing Net1 3'UTR transcript, which has previously been shown to exhibit a strong localization bias in several cell types. In order to determine if motor proteins contribute to these RNA distributions, they use motor protein inhibitors to confirm that the localization of individual members of both classes of transcripts, 5'TOP and GA-rich, is kinesin-dependent and that RNA localization to specific subcellular regions is likely to coincide with RNA localization to microtubule plus ends that concentrate in the basal side of epithelial cells as well as in neuronal processes.

In summary, Goering et al. present an interesting study that contributes to our understanding of RNA localization. While RNA localization has predominantly been studied in a single cell type or experimental system, this work looks for commonalities to explain general principles. I believe that this is an important advance, but there are several points that should be addressed.

Comments:

1) The Mili lab has previously characterized the localization of ribosomal proteins and NET1 to protrusions (Wang et al, 2017, Moissoglu et al 2019, Crisafis et al., 2020) and the role of kinesins in this localization (Pichon et al, 2021). These papers should be cited and their work discussed. I do not believe this reduces the novelty of this study and supports the generality of the RNA localization patterns to additional cellular locations in other cell types.

This was an unintentional oversight on our part, and we apologize. We have added citations for the mentioned publications and discussed our work in the context of theirs.

2) The 5'TOP motif begins with an invariant C nucleotide and mutation of this first nucleotide next to the cap has been shown to reduce translation regulation during mTOR inhibition (Avni et al, 1994 and Biberman et al 1997) and also Lapr1 binding (Lahr et al, 2017). Consequently, it is not clear to me if RPS28 initiates transcription with an A as indicated in Figure 3B. There also seems to be some differences in published CAGE datasets, but this point needs to be clarified. Additionally, it is not clear to me how the 5'TOP Firefly luciferase reporters were generated and if the transcription start site and exact 5'-ends of these constructs were determined. This is again essential to determine if it is a pyrimidine sequence in the 5'UTR that is important for localization or the 5'TOP motif and if Larp1 is directly regulating the localization by binding to the 5'TOP motif or if the effect they observe is indirect (e.g. is Larp1 also basally localized?). It should also be noted that Larp1 has been suggested to bind pyrimidine-rich sequences in the 5'UTR that are not next to the cap, but the details of this interaction are less clear (Al-Ashtal et al, 2021)

We did not fully appreciate the subtleties related to TOP motif location when we submitted this manuscript, so we thank the reviewer for pointing them out.

We also analyzed public CAGE datasets (Andersson et al, 2014 Nat Comm) and found that the start sites for both RPL7 and RPS28 were quite variable within a window of several nucleotides (as is the case for the vast majority of genes), suggesting that a substantial fraction of both do not begin with pyrimidines (Reviewer Figure 1). Yet, by smFISH, endogenous RPL7 and RPS28 are clearly basally/neurite localized (see new figure 3C).

Reviewer Figure 1. Analysis of transcription start sites for RPL7 (A) and RPS28 (B) using CAGE data (Andersson et al, 2014 Nat Comm). Both genes show a window of transcription start sites upstream of current gene models (blue bars at bottom).

A more detailed analysis of our PRRE-containing reporter transcripts led us to find that in these reporters, the pyrimidine-rich element was approximately 90 nucleotides into the body of the 5’ UTR. Yet these reporters are also basally/neurite localized. The organization of the PRRE-containing reporters is now more clearly shown in an updated figure 3D.

From these results, it would seem that the pyrimidine-rich element need not be next to the 5’ cap in order to regulate RNA localization. To generalize this result, we first used previously identified 5’ UTR pyrimidine-rich elements that had been found to regulate translation in an mTOR-dependent manner (Hsieh et al 2012). We found that, as a class, RNAs containing these motifs were similarly basally/neurite localized as RP mRNAs. These results are presented in figures 3A and 3I.

We then asked if the position of the pyrimidine-rich element within the 5’ UTR of these RNAs was related to their localization. We found no relationship between element position and transcript localization as elements within the bodies of 5’ UTRs were seemingly just as able to promote basal/neurite localization as elements immediately next to the 5’ cap. These results are presented in figures 3B and 3J.

To further confirm that pyrimidine-rich elements need not be immediately next to the 5’ cap, we redesigned our RPL7-derived reporter transcripts such that the pyrimidine-rich motif was immediately adjacent to the 5’ cap. This was possible because the reporter uses a CMV promoter that reliably starts transcription at a known nucleotide. We then compared the localization of this reporter (called “RPL7 True TOP”) to our previous reporter in which the pyrimidine-rich element was ~90 nt into the 5’ UTR (called “RPL7 PRRE”) (Reviewer Figure 2). As with the PRRE reporter, the True TOP reporter drove RNA localization in both epithelial and neuronal cells while purine-containing mutant versions of the True TOP reporter did not (Reviewer Figure 2A-D). In the epithelial cells, the True TOP was modestly but significantly better at driving basal RNA localization than the PRRE (Reviewer Figure 2E) while in neuronal cells the True TOPs were modestly but insignificantly better. Again, this suggests that pyrimidine-rich motifs need not be immediately cap-adjacent in order to regulate RNA localization.

Reviewer Figure 2. Experimental confirmation that pyrimidine-rich motif location within 5’ UTRs is not critical for RNA localization. (A) RPL7 True TOP smFISH in epithelial cells. (B) RPL7 True TOP smFISH in neuronal cells. (C) Quantification of epithelial cell smFISH in A. (D) Quantification of neuronal cell smFISH in D. (E) Comparison of the location in epithelial cells of endogenous RPL7 transcripts, RPL7 PRRE reporter transcripts, and PRL7 True TOP reporter transcripts. (F) Comparison of the neurite-enrichment of RPL7 PRRE reporters and RPL7 True TOP reporters. In C-F, the number of cells included in each analysis is shown.

In response to the point about whether the localization results are direct effects of LARP1, we did not assay the binding of LARP1 to our PRRE-containing reporters, so we cannot say for sure. However, given that PRRE-dependent localization required LARP1 and there is much evidence about LARP1 binding pyrimidine-rich elements (including those that are not cap-proximal as the reviewer notes), we believe this to be the most likely explanation.

It should also be noted here that while pyrimidine-rich motif position within the 5’ UTR may not matter, its location within the transcript does. PRREs located within 3’ UTRs were unable to direct RNA localization (Figure 5).

3) In figure 1A, they indicate that mRNA stability can contribute to RNA localization, but this point is never discussed. This may be important to their work since Larp1 has also been found to impact mRNA half-lives (Aoki et al, 2013 and Mattijssen et al 2020, Al-Ashtal et al 2021). Is it possible the effect they see when Larp1 is depleted comes from decreased stability?

We found that PRRE-containing reporter transcripts were generally less abundant than their mutant counterparts in C2bbe1, HCA7, and MDCK cells (figure 3 – figure supplements 5, 6, and 8) although the effect was not consistent in mouse neuronal cells (figure 3 – figure supplement 13).

However, we don’t think it is likely that the changes in localization are due to stability changes. This abundance effect did not seem to be LARP1-dependent as both PRRE-containing and PRRE-mutant reporters were generally more expressed in LARP1-rescue epithelial cells than in LARP1 KO cells (figure 4 – figure supplement 9).

It should be noted here that we are not ever actually measuring transcript stability but rather steady state abundances. It cannot therefore be ruled out that LARP1 is regulating the stability of our PRRE reporters. Given, though, that their localization was dependent on kinesin activity (figures 7F, 7G), we believe the most likely explanation for the localization effects is active transport.

4) Also Moor et al, 2017 saw that feeding cycles changed the localization of 5'TOP mRNAs. Similarly, does mTOR inhibition or activation or simply active translation alter the localization patterns they observe? Further evidence for dynamic regulation of RNA localization would strengthen this paper

We are very interested in this and have begun exploring it. We have data suggesting that PRREs also mediate the feeding cycle-dependent relocalization of RP mRNAs. As the reviewer says, we think this leads to a very attractive model involving mTOR, and we are currently working to test this model. However, we don’t have the room to include those results in this manuscript and would instead prefer to include them in a later manuscript that focuses on nutrient-induced dynamic relocalization.

5) For smFISH quantification, is every mRNA treated as an independent measurement so that the statistics are calculated on hundreds of mRNAs? Large sample sizes can give significant p-values but have very small differences as observe for Firefly vs. OSBPL3 localization. Since determining the biological interpretation of effect size is not always clear, I would suggest plotting RNA position per cell or only treat biological replicates as independent measurements to determine statistical significance. This should also be done for other smFISH comparisons

This is a good suggestion, and we agree that using individual puncta as independent observations will artificially inflate the statistical power in the experiment. To remedy this in the epithelial cell images, we first reanalyzed the smFISH images using each of the following as a unique observation: the mean location of all smFISH puncta in one cell, the mean location of all puncta in a field of view, and the mean location of all puncta in one coverslip. With each metric, the results we observed were very similar (Reviewer Figure 3) while the statistical power of course decreased. We therefore chose to go with the reviewer-suggested metric of mean transcript position per cell.

Reviewer Figure 3. C2bbe1 monolayer smFISH spot position analysis. RNA localization across the apicobasal axis is measured by smFISH spot position in the Z axis. This can be plotted for each spot, where thousands of spots over-power the statistics. Spot position can be averaged per cell as outlined manually within the FISH-quant software. This reduces sample size and allows for more accurate statistical analysis. When spot position is averaged per field of view, sample size further decreases, statistics are less powered but the localization trends are still robust. Finally, we can average spot position per coverslip, which represents biological replicates. We lose almost all statistical power as sample size is limited to 3 coverslips. Despite this, the localization trends are still recognizable.

When we use this metric, all results remain the same with the exception of the smFISH validation of endogenous OSBPL3 localization. That result loses its statistical significance and has now been omitted from the manuscript. All epithelial smFISH panels have been updated to use this new metric, and the number of cells associated with each observation is indicated for each sample.

For the neuronal images, these were already quantified at the per-cell level as we compare soma and neurite transcript counts from the same cell. In lieu of more imaging of these samples, we chose to perform subcellular fractionation into soma and neurite samples followed by RT-qPCR as an orthogonal technique (figure 3K, figure 3 supplement 14). This technique profiles the population average of approximately 3 million cells.

6) F: How was the segmentation of soma vs. neurites performed? It would be good to have a larger image as a supplemental figure so that it is clear the proximal or distal neurites segments are being compared

All neurite vs. soma segmentations were done manually. An example of this segmentation is included as Reviewer Figure 4. This means that often only proximal neurites segments are included in the analysis as it is often difficult to find an entire soma and an entire neurite in one field of view. However, in our experience, inclusion of more distal neurite segments would likely only strengthen the smFISH results as we often observe many molecules of localized transcripts in the distal tips of these neurites.

Reviewer Figure 4. Manual segmentation of differentiated CAD soma and neurite in FISH-quant software. Neurites that do not overlap adjacent neurites are selected for imaging. Often neurites extend beyond the field of view, limiting this assay to RNA localization in proximal neurites.

Also, it should be noted that the neuronal smFISH results are now supplemented by experiments involving subcellular fractionation and RT-qPCR (figure 3 supplement 14). These subcellular fractionation experiments collect the whole neurite, both the proximal and distal portions.

Text has been added to the methods under the header “smFISH computational analysis” to clarify how the segmentation was done.

Author Response

Reviewer #3 (Public Review):

Main results:

1) TCR convergence is different from publicity: The authors look at CDR3 sequence features of convergent TCRs in the large Emerson CMV cohort. Amino usage does not perfectly correlate with codon degeneracy, for example, arginine (which has 6 codons) is less common in convergent TCRs, whereas leucine and serine are elevated. It's argued that there's more to convergence than just recombination biases, which makes sense. (I wonder if the trends for charged amino acids could be explained by the enrichment of convergent TCRs in CD8 T cells, which tend to have more acidic CDR3 loops). There's also a claim that the overlap between convergent and public TCRs is lower in tumors with a high mutational burden (TMB), but this part is sketchy: the definition of public TCRs is murky and hard to interpret, and the correlation between TMB and convergence-publicity overlap is modest (two cohorts with low TMB have higher overlap, and the other three have lower, but there is no association over those three, if anything the trend is in the other direction). It's also not clear why the overlap between COVID19 cohort convergent TCRs and public TCRs defined by the pre-2019 Emerson cohort should be high. A confounder here is the potential association between convergence and clonal expansion since expanded clonotypes can spawn apparently convergent TCRs due to sequencing errors. The paper "TCR Convergence in Individuals Treated With Immune Checkpoint Inhibition for Cancer" (Ref#5 here) gives evidence that sequencing errors may be inflating convergence in this specific dataset.

We really appreciate the reviewer’s feedback. We respond to each of the reviewer’s points below:

(1) Amino acid preference of convergent TCRs might be caused by CD8+ T cell enrichment. To test this hypothesis, we performed the same analysis using only CD8+ T cells (using the Cader 2019 lymphoma cohort). The results are shown below. We do not observe significant changes after excluding CD4+ T cells, indicating that this enrichment might be caused by factors other than CD4/CD8 differences.

(2) Definition of public TCRs. We have changed the definition of public TCRs. Instead of mixing the Emerson cohort into each group and using the mixed cohort to define the public TCRs, we just used the 666 samples of the Emerson cohort to define the same set of public TCRs and applied them to each cohort. Both the dataset and the approach used in this manuscript is consistent with a previous study on the same topic (Madi et al., 2014, elife).

(3) Convergence-publicity overlap: We agree with the reviewer that some high TMB tumors did not show further decrease of convergence-publicity overlap. One potential explanation is that the correlation between the two is not linear. By adding additional cohorts in this revision (healthy and recovered COVID-19 patients), we confirmed the previously observed overall trend between TMB and the overlap, which supported our conclusions (see figure below). On the other hand, we believe that the high overlap of convergent TCRs among healthy cohorts might result from exposure to common antigens. In the cancer patients, while still exposed, private antigens derived from tumor cells are expected to compete for resources, thus reducing the proportion of these public TCRs in the blood repertoire. The above discussion has been added to the revised manuscript:

“Healthy individuals are expected to be exposed to common pathogens, which might induce public T cell responses. On the other hand, cancer patients have more neoantigens due to the accumulative mutation, which drives their antigen-specific T cells to recognize these 'private' antigens. This reduces the proportion of public TCRs in antigen-specific TCRs. Furthermore, a higher tumor mutation burden (TMB) would indicate a higher abundance of neoantigens, resulting in a lower ratio of public TCRs.”

2) Convergent TCRs are more likely to be antigen-specific: This is nicely shown on two datasets: the large dextramer dataset from 10x genomics, and the COVID19 datasets from Adaptive biotech. But given previous work on TCR convergence, for example, the Pogorelyy ALICE paper, and many others, this is also not super-surprising.

We thank the reviewer for bringing up this related work. In the Pogorelyy ALICE paper, the authors defined TCR neighbors based on one nucleotide difference of a given CDR3, which included both synonymous and non-synonymous changes. In other words, ALICE combines both convergence and mismatched (with hamming distance 1) sequences as neighbors. Although highly relevant, our approach is different by focusing only on the convergence, as mismatch has been extensively investigated by previous studies. We have now added this paper as Ref 27, and discussed the difference between ALICE and our method in the revised manuscript.

3) Convergent T cells exhibit a CD8+ cytotoxic gene signature: This is based on a nice analysis of mouse and human single-cell datasets. One striking finding is that convergent TCRs are WAY more common in CD8+ T cells than in CD4+ T cells. It would be interesting to know how much of this could be explained by greater clonal expansion of CD8+ T cells, together with sequencing errors. A subtle point here is that some of the P values are probably inflated by the presence of expanded clonotypes: a group of cells belonging to the same expanded clonotype will tend to have similar gene expression (and therefore similar cluster membership), and will necessarily all be either convergent or not convergent collectively since they share the same TCR. So it's probably not quite right to treat them as independent for the purposes of assessing associations between gene expression clusters and convergence (or any other TCR-defined feature). You can see evidence for clonal expansion in Figure 3C, where TRAV genes are among the most enriched, suggesting that Cluster 04 may contain expanded clones.

(1) We agree with the reviewer that a possible explanation of the CD8/CD4 difference is the larger cell expansion of CD8+ T cells. We tested this hypothesis by counting the number of T cell clones instead of cell number to remove the effect that would have been caused by CD8 T cell expansion. We first investigated the bulk TCR repertoire sequencing samples as Figure 3 - figure supplement 2C-2D (see figure below). We observed higher convergence levels for the CD8+ T cell clones compared to CD4+ T cells. The additional description of this topic was added at the last paragraph of the result section of “Convergent T cells exhibit a CD8+ cytotoxic gene signature” as follows:

“The results may be explained by larger cell expansions of CD8+ T cells than CD4+ T cells. Therefore, we calculated the number of convergent clones within CD8+ T cells and CD4+ T cells from the above datasets to exclude the effects of cell expansion. As a result, in the scRNA-seq mouse data, while only 1.54% of the CD4+ clones were convergent, 3.76% of the CD8+ clones showed convergence. Likewise, 0.17% of convergent CD4+ T cell clones and 1.03% of convergent CD8+ T cell clones were found in human scRNA-seq data. In the bulk TCR-seq lymphoma data, similar results were also observed, where the gap between the convergent levels of CD4+ and CD8+ T cells narrowed but remained significant (Figure 3—figure supplement 2C-2D). In conclusion, these results suggest that CD8+ T cells show higher levels of convergence than CD4+ T cells, which substantiated our hypothesis that convergent T cells are more likely antigen-experienced. This observation has been tested using multiple datasets with diverse sequencing platforms and sequencing depth to minimize the impact of batch or other technical artifacts.”

(2) We next investigated the effect of cell expansion in the single cell analysis. We agree with the reviewer that some highly-expanded convergent clones could inflate the p-value. Therefore, we revised the calculation of TCR convergence by using the T cell clone instead of individual cells. We observed that the clusters of interest mentioned in the paper (for both mouse and human data) remain at the top convergent level among all clusters (see table below), with p values estimated using Binomial exact test. These results supported our hypothesis that TCR convergence is enriched for T cell clusters that are more likely antigen-experienced.

4) TCR convergence is associated with the clinical outcome of ICB treatment: The associations for the first analysis are described as significant in the text, and they are, but just barely (0.045 and 0.047, but you have to check the figure to see that).

As suggested by the reviewer, we have added the p-value to the test so that it is easier to see. In this revision, we adopted another definition of convergent level, changing from the ratio of convergent TCR to the actual number of convergent T cell clones within each sample. The p-values were more significant using this new indicator (0.02 and 0.00038). To avoid the effect of other variables that might be correlative with convergent levels, especially the sequencing depth, the multivariate Cox model was used for both datasets tested in the paper, correcting for TCR clonality, TCR diversity and sequencing depth (and different treatment methods for melanomas data). As a result, convergence remains significantly prognostic after adjusting for the additional variables.

5) Introduction/Discussion: Overall, the authors could do a better job citing previous work on convergence, for example, papers from Venturi on convergent recombination and the work from Mora and Walczak (ALICE, another recombination modeling). They also present the use of convergence as an ICB biomarker as a novel finding, but Ref 5 introduces this concept and validates it in another cohort. Ref 5 also has a careful analysis of the link between sequencing errors and convergence, which could have been more carefully considered here.

We thank the reviewer for this excellent suggestion. We have added the citation of Venturi on convergent recombination as Ref 43 and we cited it at the last paragraph of the result selection:

“Convergent recombination was claimed to be the mechanistic basis for public TCR response in many previous studies(Quigley et al., 2010; Venturi et al., 2006).”

We also included work from Mora and Walczak in the fourth paragraph of the introduction and the third paragraph of the discussion as Ref 27 to introduce this TCR similarity-based clustering method as well as its application in predicting ICB response:

“This idea has led several TCR similarity-based clustering algorithms, such as ALICE (Pogorelyy et al., 2019), TCRdist (Dash et al., 2017), GLIPH2 (Huang et al., 2020), iSMART (Zhang et al., 2020), and GIANA (Zhang et al., 2021), to be developed for studying antigen-driven T cell expansion during viral infection or tumorigenesis.”

“In addition, the potential prognostic value of TCR convergence and TCR similarity-based clustering was testified in other studies(Looney et al., 2019; Pogorelyy et al., 2019).”

Ref 5 was recited while discussing the effect of sequencing error on TCR convergence in the fourth paragraph of discussion:

“Improper handling of sequencing errors may result in the overestimation of TCR convergence (Looney et al., 2019).”

Author Response

Reviewer #1 (Public Review):

Kazrin appears to be implicated in many diverse cellular functions, and accordingly, localizes to many subcellular sites. Exactly what it does is unclear. The authors perform a fairly detailed analysis of Kazrin in-cell function, and find that it is important for the perinuclear localization of TfN, and that it binds to members of the AP-1 complex (e.g., gamma-adaptin). The authors note that the C-terminus of Kazrin (which is predicted to be intrinsically disordered) forms punctate structures in the cytoplasm that colocalize with components of the endosomal machinery. Finally, the authors employ co-immunoprecipitation assays to show that both N and C-termini of Kazrin interacts with dynactin, and the dynein light-intermediate chain.

Much of the data presented in the manuscript are of fairly high quality and describe a potentially novel function for Kazrin C. However, I had a few issues with some of the language used throughout, the manner of data presentation, and some of their interpretations. Most notably, I think in its current form, the manuscript does not strongly support the authors' main conclusion: that Kazrin is a dynein-dynactin adaptor, as stated in their title. Without more direct support for this function, the authors need to soften their language. Specific points are listed below.

Major comments:

1) I agree with the authors that the data provided in the manuscript suggest that Kazrin may indeed be an endosomal adaptor for dynein-dynactin. However, without more direct evidence to support this notion, the authors need to soften their language stating as much. For example, the title as stated would need to be changed, as would much of the language in the first paragraph of the discussion. Alternatively, the manuscript could be significantly strengthened if the authors performed a more direct assay to test this idea. For example, the authors could use methods employed previously (e.g., McKenney et al., Science 2014) to this end. In brief, the authors can simply use their recombinant Kazrin C (with a GFP) to pull out dynein-dynactin from cell extracts and perform single molecule assays as previously described.

While this is certainly an excellent suggestion, the in vitro dynein/dynactin motility assays are really not straight forward experiments for laboratories that do not use them as a routine protocol. That is why we asked Dr. Thomas Surrey (Centre for Genomic Regulation, Barcelona), an expert in the biochemistry and biophysics of microtubule dynamics, to help us with this kind of analysis. In their setting, TIRF microscopy is used to follow EGFPdynein/dynactin motility along microtubules immobilized on cover slides (Jha et al., 2017). As shown in figure R1, more binding of EGFP-dynein to the microtubules is observed when purified kazrin is added to the assay (from 20 to 400 nM), but there is no increase in the number or processivity of the EGFP-dynein motility events. These results are hard to interpret at this point. Kazrin might still be an activating adaptor but a component is missing in the assay (i. e. an activating posttranslational modification or a particular subunit of the dynein or dynactin complexes), or it could increase the processivity of dyneindynactin in complex with another bona fide activating adaptor, as it has been demonstrated for LIS1 (Baumbach et al., 2017; Gutierrez et al., 2017). Alternatively, kazrin could transport dynactin and/or dynein to the microtubule plus ends in a kinesin 1-dependent manner, in order to load the peripheral endosomes with the minus end directed motor (Yamada et al., 2008).

Figure R1. Kazrin C purified from E. coli increases binding of dynein to microtubules but does not increase the number or processivity of EGFP-dynein motility events. A. TIRF (Total Internal Reflexion Fluorescence) micrographs of microtubule-coated cover slides incubated in the presence of 10 nM EGFP-dynein and 20 nM dynactin in the presence or absence of 20 nM kazrin C, expressed and purified from E. coli. B. Kymographs of TIRF movies of microtubule-coated cover slides incubated in the presence of purified 10 nM EGFP-dynein, 20 nM dynactin and either 400 nM of the activating adaptor BICD2 (1:2:40 ratio) (left panel) or kazrin C (right panel). Red squares indicate processive dynein motility events induced by BICD2”.

Investigating the molecular activity of kazrin on the dynein/dynactin motility is a whole project in itself that we feel it is out of the scope of the present manuscript. Therefore, as suggested by the BRE, we have chosen to soften the conclusions and classify kazrin as a putative “candidate” dynein/dynactin adaptor based on its interactome, domain organization and subcellular localization, as well as on the defects installed in vivo on the endosome motility upon its depletion. We also discuss other possibilities as those outlined above.

2) I'm not sure I agree with the use of the term 'condensates' used throughout the manuscript to describe the cytoplasmic Kazrin foci. 'Condensates' is a very specific term that is used to describe membraneless organelles. Given the presumed association of Kazrin with membrane-bound compartments, I think it's more reasonable to assume these foci are quite distinct from condensates.

We actually used condensates to avoid implying that the kazrin IDR generates membraneless compartments or induces liquid-liquid-phase separation, which is certainly not a conclusion from the manuscript. However, since all reviewers agreed that the word was misleading, we have substituted the term condensates for foci throughout the manuscript.

3) The authors note the localization of Tfn as perinuclear. Although I agree the localization pattern in the kazKO cells is indeed distinct, it does not appear perinuclear to me. It might be useful to stain for a centrosomal marker (such as pericentrin, used in Figure 5B) to assess Tfn/EEA1 with respect to MT minus ends.

We have now changed the term perinuclear, which implies that endosomes surround the nucleus, by the term juxtanuclear, which more accurately define what we wanted to indicate (close to). We thank the reviewer for pointing out this lack of accuracy. We also more clearly describe in the text that in fibroblast, the Golgi apparatus and the Recycling Endosomes (REs) gather around the pericentriolar region ((Granger et al., 2014) and reference therein), which is usually close to the nucleus ((Tang and Marshall, 2012) and references therein). Nevertheless, as suggested by the reviewer, we have included pictures of the TxR-Tfn and EEA1-labelled endosomes accumulating around pericentrin in wild type mouse embryonic fibroblast (MEF) (Figure 1–supplement figure 3) to illustrate these points.

4) "Treatment with the microtubule depolymerizing drug nocodazole disrupted the perinuclear localization of GFP-kazrin C, as well as the concomitant perinuclear accumulation of EE (Fig. 5C & D), indicating that EEs and GFP-kazrin C localization at the pericentrosomal region required minus end-directed microtubule-dependent transport, mostly affected by the dynactin/dynein complex (Flores-Rodriguez et al., 2011)."

• I don't agree that the nocodazole experiment indicates that minus end-directed motility is required for this perinuclear localization. In the absence of other experiments, it simply indicates that microtubules are required. It might, however, "suggest" the involvement of dynein. The same is true for the subsequent sentence ("Our observations indicated that kazrin C can be transported in and out of the pericentriolar region along microtubule tracks...").

We agree with the reviewer. To reinforce the point that GFP-kazrin C localization and the pericentriolar accumularion of EEA1 rely on dynein-dependent transport, we have now added an experiment in figure 5E and F, where we use ciliobrevin to inhibit dynein in cells expressing GFP-kazrin C. In the treated cells, we see that the GFP-kazrin C staining in the pericentrin foci is lost and that EEs have a more dispersed distribution, similar to kazKO MEF. We have also completed and rearranged the in vivo fluorescence microscopy data to more clearly show that small GFP-kazrin C foci can be observed moving towards the cell centre (Figure 5-S1 and movies 6 and 7). Taken all this data together, I think we can now suggest that kazrin might travel into the pericentriolar region, possibly along microtubules and powered by dynein.

5) Although I see a few examples of directed motion of Tfn foci in the supplemental movies, it would be more useful to see the kymographs used for quantitation (and noted by the authors on line 272). Also related to this analysis, by "centripetal trajectories", I assume the authors are referring to those moving in a retrograde manner. If so, it would be more consistent with common vernacular (and thus more clear to readers) to use 'retrograde' transport.

We have now included some more examples of the time projections used in the analysis in figure 6-S1 and 2, where we have coloured in blue the fairly straight, longer trajectories, as opposed to the more confined movements that appeared as round dots in the time projections (coloured in red). We have also added more videos illustrating the differences observed in cells expressing endogenous or GFP-kazrin C versus kazKO cells or kazKO cells expressing GFP or GFP-kazrin C-Nt. Movies 8 and 11 show the endosome motility in representative WT and kazKO cells (movie 8) and kazKO cells expressing GFP, GFPkazrin C or GFP-kazrin C Nt (movie 11). Movies 9 and 10 show endosome motility in four magnified fields of different WT and kazKO cells, where longer and faster motility events can be observed when endogenous kazrin is expressed. Movies 12 to 14 show endosome motility in four magnified fields of different kazKO cells expressing, GFP-kazrin C (movie 12), GFP (movie 13) and GFP-kazrin C-Nt (movie 14). Longer and faster movements can be observed in the different insets of movie 12, as compared with movies 13 and 14. Finally, as suggested by the reviewer, we have re-worded centripetal movement to retrograde movement throughout the manuscript.

6) The error bars on most of the plots appear to be extremely small, especially in light of the accompanying data used for quantitation. The authors state that they used SEM instead of SD, but their reasoning is not stated. All the former does is lead to an artificial reduction in the real deviation (by dividing SD by the square root of whatever they define as 'n', which isn't clear to me) of the data which I find to be misleading and very nonrepresentative of biological data. For example, the error bars for cell migration speed in Figure 2B suggest that the speeds for WT cells ranged from ~1.7-1.9 µm/sec, which I'm assuming is largely underrepresenting the range of values. Although I'm not a statistician, as someone that studies biochemical and biological processes, I strongly urge the authors to use plots and error bars that more accurately describe the data to your readers (e.g., scatter plots with standard deviation are the most transparent way to display data).

We have now changed all plots to scattered plots with standard deviations, as suggested.

Author Response

Reviewer #2 (Public Review):

Wang et al. elegantly exploit single-cell RNA-seq datasets to question the putative involvement of lncRNAs in human germ cell development. In the first part of the study, the authors use computational approaches to identify and characterize, from existing data, lncRNAs expressed in the germline. Of note, the scRNA-seq data used were generated from polyA+ RNAs, and thus non-polyadenylated lncRNAs could not be retrieved. Most of the lncRNAs identified in the germ cells and in the somatic cells of the gonads were previously unannotated. While this increases the catalog of lncRNA genes in the human genome, further characterization is needed to determine which fraction of these newly identified lncRNAs represent bona fide transcripts or transcriptional noise.

Differential expression analysis between developmental stages, sexes, or cell types led to several observations: (i) whatever the stage of development, the number of expressed lncRNAs is higher in fetal germ cells compared to gonadal somatic cells; (ii) there is a continuous increase in the number of expressed lncRNA during the development of the germline; of note, a similar, although the more subtle trend is observed for protein-coding genes; (iii) the developmental stage at which there is the highest number of lncRNA expressed differs between male and female germ cells. While convincing, the significance of these observations is difficult to assess. However, the authors remain prudent with their conclusion and are not over-interpreting their findings.

We appreciate Reviewer #2 precise summary of our analysis and highlighting the significances of these datasets for other researchers and future studies.

Interestingly, integrating lncRNA expression to classify cell types led to the identification of a novel population of cells in the female germline that had not been revealed by protein-coding gene only-based classification. The biological relevance of this population, which cluster with mitotic populations, remains to be demonstrated. Finally, by examining lncRNA biotype, the authors could demonstrate an enrichment, in the germ cells, of the antisense head-to-head organization (in relation to the nearby protein-coding gene) compared to other biotypes. Whether this is different from the general distribution of lncRNA should be discussed.

We analyzed the lncRNAs in NONCODEv5 database (human genome), and the result showed that XH type occupied 21.73% of the intragenic lncRNA-mRNA pairs in NONCODEv5 database (human genome), which is lower than 26.58% in fGC and 26.23% in mGC (Response Figure 1).

Response Figure 1. Genomic distribution and biotypes of the lncRNAs in NONCODEv5 database and lncRNAs expressed in human gonad.

In the second part of the manuscript, Wang et al focus on one pair of divergent lncRNA-protein coding genes (LNC1845-LHX8). To document the choice of this particular pair, it would be informative to have its correlation score indicated in Figure 3C. he existence of this transcript was validated using female fetal ovaries, and its function was addressed in late primordial germ cells like cells (PGCLC) derived from human embryonic stem cells (hESCs). The authors have used an admirable set of orthogonal approaches that led them to conclude as to a role for LNC1845 in regulating in cis the nearby gene LHX8. They further went on to identify the underlying mechanisms, which involve modification of the chromatin landscape through direct interaction of LNC1845 with a histone modifier. Among the different strategies used (KO, stop transcription, overexpression), the shRNA-mediated knock-down is the only one to specifically address the function of the transcript itself, as opposed to the active transcription. The result of this experiment led the authors to conclude that the LNC1845 RNA is functional, a conclusion that is reinforced by the demonstration of physical interaction between the LNC1845 RNA and WDR5, a component of MLL methyltransferase complexes. The result of the KD experiment is however puzzling as RNAi has been shown not to be the method of choice for targeting nuclear lncRNAs (Lennox et al. NAR 2016).

We thank the Reviewer #2’s suggestion to add the correlation score of LNC1845-LHX8 pair and the Pearson Correlation of this pair is 0.3268. We have added the number to Figure 4C because which the expression correlation of LNC1845 and LHX8 was first mentioned. We have compared many other similar studies, shRNA knockdown has been widely used to target nuclear lncRNAs (Guttman et al. Nature 2011; Luo et al. Cell Stem Cell 2016; Subhash et al. Nucleic Acids Res. 2018; Li et al. Genome Res 2021), and the knockdown efficiency seemed to be feasible and acceptable to be used. The knockdown results are consistent with the deletion mutation and stop transcription approaches, all three showed that LNC1845 transcriptional expression is required for proper LHX8 expression in late PGCLCs.

Overall, the functional investigation is convincing and strengthened by the inclusion of multiple clones for each approach, and by the convergence in the outcome of each individual approach. The depth of characterization is also remarkable. The analyses of the mechanisms at stake are somehow less solid, as there is less evidence demonstrating the involvement of the LNC1845 RNA and its interaction with WDR5.

We have added more experimental evidence to strengthen the model especially the interaction of LNC1845 and WDR5. Apart from the RIP-qPCR results of WDR5 demonstrating the enrichment of LNC1845 by WDR5 pulldown (Figure S8D), we performed chromatin isolation by RNA purification (ChIRP) assay using antisense oligos along the entire LNC1845 transcript sequence. ChIRP results confirmed that WDR5 protein were enriched when anti-LNC1845 oligo probes were used to isolate the complex but not the controls without the probes or without overexpression of LNC1845 transcript (Response Figure 2). Taken together, the findings of both approaches support the model that LNC1845 directly interacts with WDR5 to modulate the H3K4me3 modification for LHX8 transcriptional activation. (Related to supplementary figure 8D and 8E.)

Response Figure 2. LNC1845 binding for WDR5 was verified by CHIRP-western blot.

Altogether, this study provides a convincing demonstration of the role of a lncRNA on the regulation of a nearby gene in the context of the germline. However, to have a better understanding of the functionality of lncRNA genes in general, it would be interesting to know whether other pairs of lncRNA-PC genes have been functionally investigated in this context, where no function for the lncRNA gene could be demonstrated. Negative results are highly informative and if so, these could be included in the manuscript.

We appreciate Reviewer #2 suggestion to add other lncRNA-PC gene pairs results. In fact, we have analyzed and presented the results of another 2 pairs in figure 7D. LncRNAs LNC3346 and LNC15266 were also transcriptionally regulated by FOXP3, and they may regulate their neighbor genes TMCO1 and MPP5, as figure 7D showed. Our analysis showed that other lncRNA-PC gene pairs may also have the similar transcriptional regulation as LNC1845-LHX8 during germ cell development.

Author Response

Reviewer #2 (Public Review):

Charme is a long non-coding RNA reported by the authors in their previous studies. Their previous work, mainly using skeletal muscles as a model, showed the functional relevance of Charme, and presented data demonstrating its nuclear role, primarily via modulating the sub-nuclear localization of Matrin 3 (MATR3). Their data from skeletal muscles suggested that loss of the intronic region of Charme affects the local 3D genome organization, affecting MATR3 occupancy and this gene expression. Loss of Charme in vivo leads to cardiac defects. In this manuscript, they characterize the cardiac developmental defects and present molecular data supporting how the loss of Charme affects the cardiac transcriptome repertoire. Specifically, by performing whole transcriptome analysis in E12.5 hearts, they identify gene expression changes affected in developing hearts due to loss of Charme. Based on their previous study in skeletal muscles, they assume that Charme regulates cardiac gene expression primarily via MATR3 also in developing cardiomyocytes. They provide CLIP-seq data for MATR3 (transcriptome-wide foot printing of MATR3) in wild-type E15.5 hearts and connect the binding of MATR3 to gene expression changes observed in Charme knockout hearts. I credit the authors for providing CLIP seq data from in vivo embryonic samples, which is technically demanding.

Major strengths:

Although, as previously indicated by the authors in Charme knockout mice, the major strength is the effect of Charme on cardiac development. While the phenotype might be subtle, the functional data indicate that the role of Charme is essential for cardiac development and function. The combinatorial analysis of MATR3 CLIP-seq and transcriptional changes in the absence of Charme suggests a role of Charme that could be dependent on MATR3.

We thank this reviewer for appreciating our methodological efforts and the importance of the MATR3 CLIP-seq data from in vivo embryonic samples.

Weakness:

(i) Nuclear lncRNAs often affect local gene expression by influencing the local chromatin.

Charme locus is in close proximity to MYBPC2, which is essential for cardiac function, sarcomerogenesis, and sarcomere maintenance. It is important to rule out that the cardiac-specific developmental defects due to Charme loss are not due to (a) the influence of Charme on MYBPC2 or, of that matter, other neighboring genes, (b) local chromatin changes or enhancer-promoter contacts of MYBPC2 and other immediate neighbors (both aspects in the developmental time window when Charme expression is prominent in the heart, ideally from E11 to E15.5)

Although the cis-activity represents a mechanism-of-action for several lncRNAs, our previous work does not reveal this kind of activity for pCharme. To add stronger evidence, we have now analysed the expression of pCharme neighbouring genes in cardiac muscle. Genes were selected by narrowing the analysis not only on the genes in “linear” proximity but also on eventual chromatin contacts, which may underlie possible candidates for in cis regulation. To this purpose, we made use of the analyses that in the meantime were in progress (to answer point iv) on available Hi-C datasets (Rosa- Garrido et al. 2017). Starting from a 1 Mb region around Charme locus, we found that most of the interactions with Charme occur in a region spanning from 240 kb upstream and 115 kb downstream of Charme for a total of 370 Kb (Rev#2_Capture Fig. 1A). This region includes 39 genes, 9 of them expressed in the neonatal heart but none showing significant deregulation (see Table S2). To note, this genomic region also included the MYBPC2 locus, for which we did not find a decreased expression in the heart from our RNA-seq data (Revised Figure 2-figure supplement 1C and Table S2). This trend was confirmed through RT-qPCR analyses of several genes from E15.5 extracts, which revealed no significant difference in their abundance upon Charme ablation (Rev#2_Capture fig. 1B).

Fig. 1. A) Contact map depicting Hi-C data of left ventricular mice heart retrived from GEO accession ID GSM2544836. Data related to 1 Mb region around Charme locus were visualized using Juicebox Web App (https://aidenlab.org/juicebox/). B) RT-qPCR quantification of Charme and its neighbouring genes in CharmeWT vs CharmeKO E15.5.5 hearts. Data were normalized to GAPDH mRNA and represent means ± SEM of WT and KO (n=3) pools. Data information: p < 0.05; p < 0.01, **p < 0.001 unpaired Student’s t test.

For a better understanding, we also checked possible “local” Charme activities in skeletal muscle cells, from previous datasets (Ballarino et al., 2018). We found that in murine C2C12 cells treated with two different gapmers against Charme, three of its neighbouring genes were expressed (Josd2, Emc10 and Pold1), but none showed significant alterations in their expression levels in response to Charme knock-down (Rev#2_Capture Fig. 2).

Taken together, these results would exclude the possibility of Charme in cis activity as responsible for the phenotype.

Fig. 2: Average expression from RNA-seq (FPKM) quantification of Charme neighbouring genes in C2C12 differentiated myotubes treated with Gap-scr vs Gap-Charme. Values for Gap-Charme represent the average values of gene expression after treatment with two different gapmers (GAP-2 and GAP-2/3).

(ii) The authors provide data indicating cardiac developmental defects in Charme knockouts. Detailed developmental phenotyping is missing, which is necessary to pinpoint the exact developmental milestones affected by Charme. This is critical when reporting the cell type/ organ-specific developmental function of a newly identified regulator.

We did our best to answer this concern.

Let us first emphasise that, since their generation, we have never observed any particular tissue alteration, morphological or physiological, when dissecting the CharmeKO animals other than the muscular ones. The high specificity of pCharme expression, as also shown here by ISH (Figure 1C-D, Figure 1-figure supplement 1A-B, Figure 3A), together with the minimal alteration applied to the locus for CRISPR-Cas-mediated KO (PolyA insertion), strongly excludes the presence of an alteration in other tissues and their involvement in the development of the phenotype.

Nevertheless, we now add more developmental details to the cardiac phenotype (see also Essential revision point 2).

1- First of all, gene expression analyses performed at 12.5E, 15.5E, 18.5E and neonatal (PN2) stages allowed us to identify, at the molecular level, the developmental time point when CharmeKO effects on the cardiac muscle can be found. Our new results clearly indicate that the pCharme-mediated regulation of morphogenic and cardiac differentiation genes is detectable from E15.5 fetal stage onward (Rev#2_Capture Fig. 3/Revised Figure 2E). Together with the analysis of pCharme targets and coherently with the altered cardiac maturation and performance, this evidence is also supported by the analysis of the myosins Myh6/Myh7 ratio, which diminution in CharmeKO hearts starts from E15.5 up to 69% of control levels at PN stages (Revised Figure 2F).

2- Hematoxylin-eosin staining of dorso-ventral cryosections from CharmeWT and CharmeKO hearts confirmed the fetal malformation at the E15.5 stage (Revised Figure 2G). Moreover, the hypotrabeculation phenotype of CharmeKO hearts, which was initially examined by immunofluorescence, now finds confirmation by the analysis of key trabecular markers (Irx3 and Sema3a), which expression significantly decreases upon pCharme ablation (Rev#1_Capture Fig. 3B/Revised Figure 2-figure supplement 1G).

3- Finally, the gene expression analysis on Ki-67, Birc5 and Ccna2 (Revised Figure 2-figure supplement 1E) definitively rules out the influence of pCharme ablation on cell-cycle genes and cardiomyocytes proliferation, thus allowing a more careful interpretation of the embryonic phenotype. Note that, coherently with the lncRNA implication at later stages of development, the expression of important cardiac regulators, such as Gata4, Nkx2-5 and Tbx5, is not altered by its ablation at any of the tested time points (Rev#2_Capture Fig.3), while pCharme absence mainly affects genes which are expressed downstream of these factors.

These new results have been included in the revised version of the manuscript and better discussed.

Fig. 3: RT-qPCR quantification Gata4, Nkx2-5 and Tbx5 in CharmeWT and CharmeKO cardiac extract at E12.5, E15.5 and E18.5 days of embryonal development. Data were normalized to GAPDH mRNA and represent means ± SEM of WT and KO (n=3) pools.

(iii) Along the same line, at the molecular level, the authors provide evidence indicating a change in the expression of genes involved in cardiogenesis and cardiac function. Based on changes in mRNA levels of the genes affected due to loss of Charme and based on immunofluorescence analysis of a handful of markers, they propose a role of Charme in cell cycle and maturation. Such claims could be toned down or warrant detailed experimental validation.

See above, response to Reviewer #2 (Public Review) weakness (ii).

(iv) Authors extrapolate the mechanistic finding in skeletal muscle they reported for Charme to the developing heart. While the data support this hypothesis, it falls short in extending the mechanistic understanding of Charme beyond the papers previously published by the authors. CLIP-seq data is a step in the right direction. MATR3 is a relatively abundant RBP, binding transcriptome-wide, mainly in the intronic region, based on currently available CLIP-seq data, as well as shown by the authors' own CLIP seq in cardiomyocytes. It is also shown to regulate pre-mRNA splicing/ alternative splicing along with PTB (PMID: 25599992) and 3D genome organization (PMID: 34716321). In addition, the authors propose a MATR3 depending molecular function for Charme primarily dependent on the intronic region of Charme and due to the binding of MATR3. Answering the following question would enable a better mechanistic understanding of how Charme controls cardiac development.

(i) what are the proximal genomic regions in the 3D space to Charme locus in embryonic cardiomyocytes? Authors can re-analysis published Hi-C data sets from embryonic cardiomyocytes or perform a 4-C experiment using Charme locus for this purpose.

See above, response to Reviewer #2 (Public Review) weakness (i).

(ii) does the loss of Charme affect the splicing landscape of MATR3 bound pre-mRNAs in E12.5 ventricles in general and those arising from the NCTC region specifically?

This is an intriguing issue, as also highlighted by new evidence showing that the reactivation of fetal-specific RNA-binding proteins, including MATR3, in the injured heart drives transcriptome-wide switches through the regulation of early steps of RNA transcription and processing (D'Antonio et al., 2022).

Using the rMATS software on our neonatal RNA-Seq datasets we then investigated the effect of pCharme depletion on splicing, with a focus on NCTC. As shown in the Rev#2_Capture Fig.4A, all classical splicing alterations were investigated, such as exon-skipping, alternative 5’ splice site, alternative 3’ splice site, mutually excluded exons and intron retention. Intriguingly, we did observe a slight alteration in the splicing patterns, in particular considering exon skipping events (62% corresponding to 381 genes). Among them, the majority corresponded to exon exclusion events (237 events = 209 genes) while a smaller fraction to exon inclusion (144 events = 133 genes). Moreover, by intersecting these genes with the MATR3-bound RNAs we found a slightly significant enrichment (p=0,038) for exon inclusion (Rev#2_Capture Fig.4B).

Regarding the NCTC locus, we demonstrate that in hearts pCharme acts through different target genes. Indeed, none of the NCTC-arising transcripts are bound by MATR3 (see Table S4) or substrate for alternative splicing regulation.

While these results are very interesting for deepening the investigation of pCharme/MATR3 interplay, their biological significance needs to be further investigated through one-by-one analysis of specific transcripts. As a prosecution of the project, Nanopore sequencing of these samples on a MinION platform is currently undergoing in the lab to obtain a better characterization of alternative splicing events in response to the lncRNA ablation during development.

Fig. 4: A) Left and middle panel: Pie Chart depicting the proportion of significantly altered (FDR < 0.05) splicing events detected by rMATS comparing neonatal CharmeWT and CharmeKO RNA-seq samples. All classical splicing alterations were investigated, such as exon-skipping, alternative 3’ splice site (A3SS), intron retention, alternative 5’ splice site (A5SS) and mutually excluded exons (MXE). Right panel. Volcano plot depicting significant exon skipping events in CharmeKO (FDR < 0.05, PSI<0 for excluded and included exons, FDR >= 0.05 for invariant exons). X-axis represent exon-inclusion ratio or Percentage Spliced In (PSI) while y-axis represent –log10 of p-value. B) Pie charts representing the fraction of transcripts with at least one significant excluded (left panel), invariant (middle panel) and included (right panel) exons that are bound by MATR3. P-values of MATR3 targets enrichment for each comparison is depicted below. Statistical significance was assessed with Fisher exact test.

(iii) MATR3 binds DNA, as also shown by authors in previous studies. Is the MATR3 genomic binding altered by Charme loss in cardiomyocytes globally, as well as on the loci differentially expressed in Charme knockout heart? Overlapping MATR3 genomic binding changes and transcriptome binding changes to differentially expressed genes in the absence of Charme would better clarify the MATR3-centric mechanisms proposed here. Further connecting that to 3D genome changes due to Charme loss could provide needed clarity to the mechanistic model proposed here.

Previous experience from our (Desideri et al., 2020) and other labs (Zeitz et al 2009 J Cell Biochem), indicate that Chromatin IP is not the most suitable approach for identifying MATR3 specific targets because of the broad distribution of MATR3 over the genome. Given the number of animals that would need to be sacrificed, we moved further to strengthen our MATR3 CLIP evidence by adding the i) CharmeKO MATR3 CLIP-seq control and the ii) combinatorial analysis of MATR3 CLIP-seq with the RNA-seq data.

We have better explained the reasoning within the text, which now reads “The known ability of MATR3 to interact with both DNA and RNA and the high retention of pCharme on the chromatin may predict the presence of chromatin and/or specific transcripts within these MATR3-enriched condensates. In skeletal muscle cells, we have previously observed on a genome-wide scale, a global reduction of MATR3 chromatin binding in the absence of pCharme (Desideri et al., 2020). Nevertheless, the broad distribution of the protein over the genome made the identification of specific targets through MATR3-ChIP challenging.” (lines 274-279).

Indeed, we found that MATR3 binding was significantly decreased on numerous peaks (434/626), while its increase was observed on a smaller fraction of regions (192/626) (Revised Figure 5C). As a control, we performed MATR3 motif enrichment analysis on the differentially bound regions revealing its proximity to the peak summit (+/- 50 nt) (Revised Figure 5-figure supplement 1D) close to the strongest enrichment of MATR3, further confirming a direct and highly specific binding of the protein to these sites. To better characterise the relationship between MATR3 and pCharme, we then intersected the newly identified regions with the MATR3-bound transcripts whose expression was altered by Charme depletion. While gain peaks were equally distributed across DEGs, loss peaks were significantly enriched in a subset of pCharme down-regulated DEGs (Revised Figure 5D), suggesting a crosstalk between the lncRNA and the protein in regulating the expression of this specific group of genes. Interestingly, these RNAs mainly distribute across the same GO categories as pCharme downregulated DEGs and include genes, such as Cacna1c, Notch3, Myo18B and Rbm20 involved in embryo development and validated as pCharme/Matr3 targets in primary cardiac cells (Revised Figure 5D, lower panel and 5E)

Author Response

Reviewer 2 (Public Review):

1) The authors developed a novel C.elegans model for studying extracellular amyloid beta aggregation and is therefore likely to be taken up broadly by the field. However, the new model should be fully characterized. Throughout the manuscript, the only method to detect amyloid deposition was the GFP fluorescence intensity and morphology, while direct characterization of amyloid aggregates is lacking.

We thank the reviewer for the feedback and the foresight that this model might be taken up by the field. To strengthen our model, as the reviewer had suggested, we confirmed that the GFP fluorescence is indeed amyloid aggregations. Please, see point 3 above and the new Supporting Figure 1.1.

2) A targeted RNA interference (RNAi) screen was used to identify the key regulators of Aβ aggregation and clearance, which is one of the strengths of the study. There should be evidence that RNAi works to knockdown the specific genes. Similarly, there should be evidence indicating that ADM-2 is indeed expressed in the overexpression experiments.

We aimed to verify our main hits (cri-2 and adm-2) with a mutation in these genes, as RNAi can have off-target effects. The adm-2(ok3178) allele is a 989 bp deletion leading to a splice/acceptor change leading to a probably truncated and out-of-frame protein.

Author response image 1.

The cri-2(gk314) allele is a 1213 bp deletion covering the whole cri-2 locus, suggesting to be a null allele.

Author response image 2.

For the overexpression, there is no ADM-2 antibody available. We tried to generate an ADM-2 antibody, unfortunately unsuccessfully. Thus, we can only, based on the induction and higher red fluorescence of ADM-2::mScarlet (Supporting Figure 6.1.) infer the ADM-2 overexpression.

3) It remains unknown whether ADM-2 directly degrades Aβ or facilitates the clearance of Aβ by remoulding the ECM. The effect of ADM-2 on ECM remodeing should be examined.

We addressed this in point 1 above and also in our discussion section.

Author Response

Reviewer #2 (Public Review):

The time-dependency of the model simulations was not analyzed, and the nature of the observed biphasic time-dependent APAP response remains elusive. It would be interesting to see how the model can explain the time course of the APAP stimulation experiment.

The alternative model at its current state can only describe steady state conditions. However, we understand that the reviewer is interested in the dynamic behavior of the model. However, our approach provides a proof of principle that the alternative model can phenomenologically explain the changes of YAP localization as a response to APAP treatment. The question of how to model Hippo pathway in a time-dependent manner as a response to APAP treatment is very challenging and would require further investigations and, most notably, further development of the PDE simulation algorithms and the SME software. Hence, a technical update of the software algorithms would be required, which cannot be in the scope of this manuscript.

Nevertheless, we decided to share our first and preliminary analyses on dynamic processes caused by APAP with the reviewer. For this, we simulated the steady state model in an arbitrary manner, where APAP initiates (early time-point) and slows down (late time-points) YAP phosphorylation in the nucleus (see Figure below).

The simulated alternative model shows that increased YAP phosphorylation about 50% leads to the cytoplasmic localization of YAP (Rebuttal Figure R5A/B). However, this shuttling is not detectable in our protein fractionation and live-cell imaging experiments (see also Rebuttal Figure R7C/D). At late time points, decreasing YAP phosphorylation (about 60%) led to a clear nuclear enrichment and dephosphorylation of YAP was observed in our experiments. Thus, our mathematical model nicely describes cellular events of Hippo pathway dynamics observed at later stages after APAP treatment (nuclear enrichment). However, early events cannot be completely explained (suggested nuclear YAP exclusion is not detectable).

We suggest two explanations for this observation. First, other molecular mechanisms (not yet identified and therefore not part of the model topology) oppose the exclusion YAP enrichment that is expected at early time points. Second, detection methods used in this study (Western Blotting and life cell imaging) cannot capture minimal changes and cellular heterogeneity in the chosen experimental setup. We clarify this aspect/limitation of our study in the discussion chapter of the manuscript. Page 12, lines 436-440

Time-dependency of YAP (orange) localization based on the simulated APAP treatment. (A): Simulated control (ctrl) and APAP treatment for 2 and 48h. The treatment was simulated by changing the phosphorylation coefficient of YAP in the nucleus. (B): Simulated pYAP/YAP ratio during control and APAP treatment for 2 and 48 hours at the steady state of the model. (C): Simulated NCR of the total YAP during control and APAP treatment for 2 and 48 hours at the steady state.

Author Response

Reviewer #1 (Public Review):

Because of the importance of brain and cognitive traits in human evolution, brain morphology and neural phenotypes have been the subject of considerable attention. However, work on the molecular basis of brain evolution has tended to focus on only a handful of species (i.e., human, chimp, rhesus macaque, mouse), whereas work that adopts a phylogenetic comparative approach (e.g., to identify the ecological correlates of brain evolution) has not been concerned with molecular mechanism. In this study, Kliesmete, Wange, and colleagues attempt to bridge this gap by studying protein and cis-regulatory element evolution for the gene TRNP1, across up to 45 mammals. They provide evidence that TRNP1 protein evolution rates and its ability to drive neural stem cell proliferation are correlated with brain size and/or cortical folding in mammals, and that activity of one TRNP1 cis-regulatory element may also predict cortical folding.

There is a lot to like about this manuscript. Its broad evolutionary scope represents an important advance over the narrower comparisons that dominate the literature on the genetics of primate brain evolution. The integration of molecular evolution with experimental tests for function is also a strength. For example, showing that TRNP1 from five different mammals drives differences in neural stem cell proliferation, which in turn correlate with brain size and cortical folding, is a very nice result. At the same time, the paper is a good reminder of the difficulty of conclusively linking macroevolutionary patterns of trait evolution to molecular function. While TRNP1 is a moderate outlier in the correlation between rate of protein evolution and brain morphology compared to 125 other genes, this result is likely sensitive to how the comparison set is chosen; additionally, it's not clear that a correlation with evolutionary rate is what should be expected. Further, while the authors show that changes in TRNP1 sequence have functional consequences, they cannot show that these changes are directly responsible for size or folding differences, or that positive selection on TRNP1 is because of selection on brain morphology (high bars to clear). Nevertheless, their findings contribute strong evidence that TRNP1 is an interesting candidate gene for studying brain evolution. They also provide a model for how functional follow-up can enrich sequence-based comparative analysis.

We thank the reviewer for the positive assessment. With respect to our set of control genes and the interpretation of the correlation between the evolution of the TRNP1 protein sequence and the evolution of brain size and gyrification, we would like to mention the following: we do think that the set is small, but we took all similarly sized genes with one coding exon that we could find in all 30 species. Furthermore, the control genes are well comparable to TRNP1 with respect to alignment quality and average omega (Figure 1-figure supplement 3). Hence, we think that the selection procedure and the actual omega distribution make them a valid, unbiased set to which TRNP1’s co-evolution with brain phenotypes can be compared to. Moreover, we want to point out that by using Coevol, we correlate evolutionary rates, that is the rate of protein evolution of TRNP1 as measured with omega and the rate of brain size evolution that is modeled in Coevol as a Brownian motion process. We think that this was unclear in the previous version of our manuscript, and appreciate that the reviewer saw some merit in our analyses in spite of it.

Finding conclusive evidence to link molecular evolution to concrete phenotypes is indeed difficult and necessarily inferential. This said, we still believe that correlating rates of evolution of phenotype and sequence across a phylogeny is one of the most convincing pieces of evidence available.

Reviewer #2 (Public Review):

In this paper, Kliesmete et al. analyze the protein and regulatory evolution of TRNP1, linking it to the evolution of brain size in mammals. We feel that this is very interesting and the conclusions are generally supported, with one concern.

The comparison of dN/dS (omega) values to 125 control proteins is helpful, but an important factor was not controlled. The fraction of a protein in an intrinsically disordered region (IDR) is potentially even more important in affecting dN/dS than the protein length or number of exons. We suggest comparing dN/dS of TRNP1 to another control set, preferably at least ~500 proteins, which have similar % IDR.

Thank you for this interesting suggestion. As mentioned in the public response to Reviewer #1, we are sorry that we did not explain the rationale of the approach very well in the previous version of the manuscript. As also argued above, we think that our control proteins are an unbiased set as they have a comparable alignment quality and an average omega (dN/dS) similar to TRNP1 (Figure 1-figure supplement 3). While IDR domains tend to have a higher omega than their respective non-IDR counterparts, we do not think that the IDR content should be more relevant than omega itself as we do not interpret this estimate on its own, but its covariance with the rate of phenotypic change. Indeed, the proteins of our control set that have a higher IDR content (D2P2, Oates et al. 2013) do not show stronger evidence to be coevolving with the brain phenotypes (IDR content vs. absolute brain size-omega partial correlation: Kendall's tau = 0.048, p-value = 0.45; IDR content vs. absolute GI-omega partial correlation: Kendall’s tau = -0.025, p-value = 0.68; 88 proteins (71%) contain >0% IDRs; 8 proteins contain >62% (TRNP1 content) IDRs.

Reviewer #3 (Public Review):

In this work, Z. Kliesmete, L. Wange and colleagues investigate TRNP1 as a gene of potential interest for the evolution of the mammalian cortex. Previous evidence suggests that TRNP1 is involved in self-renewal, proliferation and expansion in cortical cells in mouse and ferret, making this gene a good candidate for evolutionary investigation. The authors designed an experimental scheme to test two non-exclusive hypotheses: first, that evolution of the TRNP1 protein is involved in the apparition of larger and more convoluted brains; and second, that regulation of the TRNP1 gene also plays a role in this process alongside protein evolution.

The authors report that the rate of TRNP1 protein evolution is strongly correlated to brain size and gyrification, with species with larger and more convoluted brains having more divergent sequences at this gene locus. The correlation with body mass was not as strong, suggesting a functional link between TRNP1 and brain evolution. The authors directly tested the effects of sequence changes by transfecting the TRNP1 sequences from 5 different species in mouse neural stem cells and quantifying cell proliferation. They show that both human and dolphin sequences induce higher proliferation, consistent with larger brain sizes and gyrifications in these two species. Then, the authors identified six potential cis-regulatory elements around the TRNP1 gene that are active in human fetal brain, and that may be involved in its regulation. To investigate whether sequence evolution at these sites results in changes in TRNP1 expression, the authors performed a massively parallel reporter assay using sequences from 75 mammals at these six loci. The authors report that one of the cis-regulatory elements drives reporter expression levels that are somewhat correlated to gyrification in catarrhine monkeys. Consistent with the activity of this cis-regulatory sequence in the fetal brain, the authors report that this element contains binding sites for TFs active in brain development, and contains stronger binding sites for CTCF in catarrhine monkeys than in other species. However, the specificity or functional relevance of this signal is unclear.

Altogether, this is an interesting study that combines evolutionary analysis and molecular validation in cell cultures using a variety of well-designed assays. The main conclusions - that TRNP1 is likely involved in brain evolution in mammals - are mostly well supported, although the involvement of gene regulation in this process remains inconclusive.

Strengths:

• The authors have done a good deal of resequencing and data polishing to ensure that they obtained high-quality sequences for the TRNP1 gene in each species, which enabled a higher confidence investigation of this locus.

• The statistical design is generally well done and appears robust.

• The combination of evolutionary analysis and in vivo validation in neural precursor cells is interesting and powerful, and goes beyond the majority of studies in the field. I also appreciated that the authors investigated both protein and regulatory evolution at this locus in significant detail, including performing a MPRA assay across species, which is an interesting strategy in this context.

Weaknesses:

• The authors report that TRNP1 evolves under positive selection, however this seems to be the case for many of the control proteins as well, which suggests that the signal is non-specific and possibly due to misspecifications in the model.

• The evidence for a higher regulatory activity of the intronic cis-regulatory element highlighted by the authors is fairly weak: correlation across species is only 0.07, consistent with the rapid evolution of enhancers in mammals, and the correlation in catarrhine monkeys is seems driven by a couple of outlier datapoints across the 10 species. It is unclear whether false discovery rates were controlled for in this analysis.

• The analysis of the regulatory content in this putative enhancer provides some tangential evidence but no reliable conclusions regarding the involvement of regulatory changes at this locus in brain evolution.

We thank the reviewer for the detailed comments. Indeed, TRNP1 overall has a rather average omega value across the tree and hence also the proportion of sites under selection is not hugely increased compared to the control proteins. This is good because we want to have comparable power to detect a correlation between the rate of protein evolution (omega) and the rate of brain size or GI evolution for TRNP1 and the control proteins. Indeed, what makes TRNP1 special is the rather strong correlation between the rate of brain size change and omega, which was only stronger in 4% of our control proteins. Hence, we do not agree with the weakness of model misspecification for TRNP1 protein evolution.

We agree that the correlation of the activity induced by the intronic cis regulatory element (CRE) with gyrification is weak, but we dispute that the correlation is due to outliers (see residual plot below) or violations of model assumptions (see new permutation analysis in the Results section). There are many reasons why we would expect such a correlation not to be weak, including that a MPRA takes the CRE out of its natural genomic context. Our conclusions do not solely rest on those statistics, but also on independent corroborating evidence: Reilly et al (2015) found a difference in the activity of the TRNP1 intron between human and macaque samples during brain development. Furthermore, we used their and other public data to show that the intron CRE is indeed active in humans and bound by CTCF (new Figure 4 - figure supplement 2).

We believe that the combined evidence suggests a likely role for the intron CRE for the co-evolution of TRNP1 with gyrification.

Author Response

Reviewer #1 (Public Review):

Trudel and colleagues aimed to uncover the neural mechanisms of estimating the reliability of the information from social agents and non-social objects. By combining functional MRI with a behavioural experiment and computational modelling, they demonstrated that learning from social sources is more accurate and robust compared with that from non-social sources. Furthermore, dmPFC and pTPJ were found to track the estimated reliability of the social agents (as opposed to the non-social objects). The strength of this study is to devise a task consisting of the two experimental conditions that were matched in their statistical properties and only differed in their framing (social vs. non-social). The novel experimental task allows researchers to directly compare the learning from social and non-social sources, which is a prominent contribution of the present study to social decision neuroscience.

Thank you so much for your positive feedback about our work. We are delighted that you found that our manuscript provided a prominent contribution to social decision neuroscience. We really appreciate your time to review our work and your valuable comments that have significantly helped us to improve our manuscript further.

One of the major weaknesses is the lack of a clear description about the conceptual novelty. Learning about the reliability/expertise of social and non-social agents has been of considerable concern in social neuroscience (e.g., Boorman et al., Neuron 2013; and Wittmann et al., Neuron 2016). The authors could do a better job in clarifying the novelty of the study beyond the previous literature.

We understand the reviewer’s comment and have made changes to the manuscript that, first, highlight more strongly the novelty of the current study. Crucially, second, we have also supplemented the data analyses with a new model-based analysis of the differences in behaviour in the social and non-social conditions which we hope makes clearer, at a theoretical level, why participants behave differently in the two conditions.

There has long been interest in investigating whether ‘social’ cognitive processes are special or unique compared to ‘non-social’ cognitive processes and, if they are, what makes them so. Differences between conditions could arise during the input stage (e.g. the type of visual input that is processed by social and non-social system), at the algorithm stage (e.g. the type of computational principles that underpin social versus non-social processes) or, even if identical algorithms are used, social and non-social processes might depend on distinct anatomical brain areas or neurons within brain areas. Here, we conducted multiple analyses (in figures 2, 3, and 4 in the revised manuscript and in Figure 2 – figure supplement 1, Figure 3 – figure supplement 1, Figure 4 – figure supplement 3, Figure 4 – figure supplement 4) that not only demonstrated basic similarities in mechanism generalised across social and non-social contexts, but also demonstrated important quantitative differences that were linked to activity in specific brain regions associated with the social condition. The additional analyses (Figure 4 – figure supplement 3, Figure 4 – figure supplement 4) show that differences are not simply a consequence of differences in the visual stimuli that are inputs to the two systems1, nor does the type of algorithm differ between conditions. Instead, our results suggest that the precise manner in which an algorithm is implemented differs when learning about social or non-social information and that this is linked to differences in neuroanatomical substrates.

The previous studies mentioned by the reviewer are, indeed, relevant ones and were, of course, part of the inspiration for the current study. However, there are crucial differences between them and the current study. In the case of the previous studies by Wittmann, the aim was a very different one: to understand how one’s own beliefs, for example about one’s performance, and beliefs about others, for example about their performance levels, are combined. Here, however, instead we were interested in the similarities and differences between social and non-social learning. It is true that the question resembles the one addressed by Boorman and colleagues in 2013 who looked at how people learned about the advice offered by people or computer algorithms but the difference in the framing of that study perhaps contributed to authors’ finding of little difference in learning. By contrast, in the present study we found evidence that people were predisposed to perceive stability in social performance and to be uncertain about non-social performance. By accumulating evidence across multiple analyses, we show that there are quantitative differences in how we learn about social versus non-social information, and that these differences can be linked to the way in which learning algorithms are implemented neurally. We therefore contend that our findings extend our previous understanding of how, in relation to other learning processes, ‘social’ learning has both shared and special features.

We would like to emphasize the way in which we have extended several of the analyses throughout the revision. The theoretical Bayesian framework has made it possible to simulate key differences in behaviour between the social and non-social conditions. We explain in our point-by-point reply below how we have integrated a substantial number of new analyses. We have also more carefully related our findings to previous studies in the Introduction and Discussion.

Introduction, page 4:

[...] Therefore, by comparing information sampling from social versus non-social sources, we address a long-standing question in cognitive neuroscience, the degree to which any neural process is specialized for, or particularly linked to, social as opposed to non-social cognition 2–9. Given their similarities, it is expected that both types of learning will depend on common neural mechanisms. However, given the importance and ubiquity of social learning, it may also be that the neural mechanisms that support learning from social advice are at least partially specialized and distinct from those concerned with learning that is guided by nonsocial sources. However, it is less clear on which level information is processed differently when it has a social or non-social origin. It has recently been argued that differences between social and non-social learning can be investigated on different levels of Marr’s information processing theory: differences could emerge at an input level (in terms of the stimuli that might drive social and non-social learning), at an algorithmic level or at a neural implementation level 7. It might be that, at the algorithmic level, associative learning mechanisms are similar across social and non-social learning 1. Other theories have argued that differences might emerge because goal-directed actions are attributed to social agents which allows for very different inferences to be made about hidden traits or beliefs 10. Such inferences might fundamentally alter learning about social agents compared to non-social cues.

Discussion, page 15:

[…] One potential explanation for the assumption of stable performance for social but not non-social predictors might be that participants attribute intentions and motivations to social agents. Even if the social and non-social evidence are the same, the belief that a social actor might have a goal may affect the inferences made from the same piece of information 10. Social advisors first learnt about the target’s distribution and accordingly gave advice on where to find the target. If the social agents are credited with goal-directed behaviour then it might be assumed that the goals remain relatively constant; this might lead participants to assume stability in the performances of social advisors. However, such goal-directed intentions might not be attributed to non-social cues, thereby making judgments inherently more uncertain and changeable across time. Such an account, focussing on differences in attribution in social settings aligns with a recent suggestion that any attempt to identify similarities or differences between social and non-social processes can occur at any one of a number of the levels in Marr’s information theory 7. Here we found that the same algorithm was able to explain social and non-social learning (a qualitatively similar computational model could explain both). However, the extent to which the algorithm was recruited when learning about social compared to non-social information differed. We observed a greater impact of uncertainty on judgments about social compared to non-social information. We have shown evidence for a degree of specialization when assessing social advisors as opposed to non-social cues. At the neural level we focused on two brain areas, dmPFC and pTPJ, that have not only been shown to carry signals associated with belief inferences about others but, in addition, recent combined fMRI-TMS studies have demonstrated the causal importance of these activity patterns for the inference process […]

Another weakness is the lack of justifications of the behavioural data analyses. It is difficult for me to understand why 'performance matching' is suitable for an index of learning accuracy. I understand the optimal participant would adjust the interval size with respect to the estimated reliability of the advisor (i.e., angular error); however, I am wondering if the optimal strategy for participants is to exactly match the interval size with the angular error. Furthermore, the definitions of 'confidence adjustment across trials' and 'learning index' look arbitrary.

First, having read the reviewer’s comments, we realise that our choice of the term ‘performance matching’ may not have been ideal as it indeed might not be the case that the participant intended to directly match their interval sizes with their estimates of advisor/predictor error. Like the reviewer, our assumption is simply that the interval sizes should change as the estimated reliability of the advisor changes and, therefore, that the intervals that the participants set should provide information about the estimates that they hold and the manner in which they evolve. On re-reading the manuscript we realised that we had not used the term ‘performance matching’ consistently or in many places in the manuscript. In the revised manuscript we have simply removed it altogether and referred to the participants’ ‘interval setting’.

Most of the initial analyses in Figure 2a-c aim to better understand the raw behaviour before applying any computational model to the data. We were interested in how participants make confidence judgments (decision-making per se), but also how they adapt their decisions with additional information (changes or learning in decision making). In the revised manuscript we have made clear that these are used as simple behavioural measures and that they will be complemented later by more analyses derived from more formal computational models.

In what we now refer to as the ‘interval setting’ analysis (Figure 2a), we tested whether participants select their interval settings differently in the social compared to non-social condition. We observe that participants set their intervals closer to the true angular error of the advisor/predictor in the social compared to the non-social condition. This observation could arise in two ways. First, it could be due to quantitative differences in learning despite general, qualitative similarity: mechanisms are similar but participants differ quantitatively in the way that they learn about non-social information and social information. Second, it could, however, reflect fundamentally different strategies. We tested basic performance differences by comparing the mean reward between conditions. There was no difference in reward between conditions (mean reward: paired t-test social vs. non-social, t(23)= 0.8, p=0.4, 95% CI= [-0.007 0.016]), suggesting that interval setting differences might not simply reflect better or worse performance in social or non-social contexts but instead might reflect quantitative differences in the processes guiding interval setting in the two cases.

In the next set of analyses, in which we compared raw data, applied a computational model, and provided a theoretical account for the differences between conditions, we suggest that there are simple quantitative differences in how information is processed in social and nonsocial conditions but that these have the important impact of making long-term representations – representations built up over a longer series of trials – more important in the social condition. This, in turn, has implications for the neural activity patterns associated with social and non-social learning. We, therefore, agree with the reviewer, that one manner of interval setting is indeed not more optimal than another. However, the differences that do exist in behaviour are important because they reveal something about the social and non-social learning and its neural substrates. We have adjusted the wording and interpretation in the revised manuscript.

Next, we analysed interval setting with two additional, related analyses: interval setting adjustment across trials and derivation of a learning index. We tested the degree to which participants adjusted their interval setting across trials and according to the prediction error (learning index, Figure f); the latter analysis is very similar to a trial-wise learning rate calculated in previous studies11. In contrast to many other studies, the intervals set by participants provide information about the estimates that they hold in a simple and direct way and enable calculation of a trial-wise learning index; therefore, we decided to call it ‘learning index’ instead of ‘learning rate’ as it is not estimated via a model applied to the data, but instead directly calculated from the data. Arguably the directness of the approach, and its lack of dependence on a specific computational model, is a strength of the analysis.

Subsequently in the manuscript, a new analysis (illustrated in new Figure 3) employs Bayesian models that can simulate the differences in the social and non-social conditions and demonstrate that a number of behavioural observations can arise simply as a result of differences in noise in each trial-wise Bayesian update (Figure 3 and specifically 3d; Figure 3 – figure supplement 1b-c). In summary, the descriptive analyses in Figure 2a-c aid an intuitive understanding of the differences in behaviour in the social and non-social conditions. We have then repeated these analyses with Bayesian models incorporating different noise levels and showed that in such a way, the differences in behaviour between social and non-social conditions can be mimicked (please see next section and manuscript for details).

We adjusted the wording in a number of sections in the revised manuscript such as in the legend of Figure 2 (figures and legend), Figure 4 (figures and legend).

Main text, page 5:

The confidence interval could be changed continuously to make it wider or narrower, by pressing buttons repeatedly (one button press resulted in a change of one step in the confidence interval). In this way participants provided what we refer to as an ’interval setting’.

We also adjusted the following section in Main text, page 6:

Confidence in the performance of social and non-social advisors

We compared trial-by-trial interval setting in relation to the social and non-social advisors/predictors. When setting the interval, the participant’s aim was to minimize it while ensuring it still encompassed the final target position; points were won when it encompassed the target position but were greater when it was narrower. A given participant’s interval setting should, therefore, change in proportion to the participant’s expectations about the predictor’s angular error and their uncertainty about those expectations. Even though, on average, social and non-social sources did not differ in the precision with which they predicted the target (Figure 2 – figure supplement 1), participants gave interval settings that differed in their relationships to the true performances of the social advisors compared to the non-social predictors. The interval setting was closer to the angular error in the social compared to the non-social sessions (Figure 2a, paired t-test: social vs. non-social, t(23)= -2.57, p= 0.017, 95% confidence interval (CI)= [-0.36 -0.4]). Differences in interval setting might be due to generally lower performance in the nonsocial compared to social condition, or potentially due to fundamentally different learning processes utilised in either condition. We compared the mean reward amounts obtained by participants in the social and non-social conditions to determine whether there were overall performance differences. There was, however, no difference in the reward received by participants in the two conditions (mean reward: paired t-test social vs. non-social, t(23)= 0.8, p=0.4, 95% CI= [-0.007 0.016]), suggesting that interval setting differences might not simply reflect better or worse performance

Discussion, page 14:

Here, participants did not match their confidence to the likely accuracy of their own performance, but instead to the performance of another social or non-social advisor. Participants used different strategies when setting intervals to express their confidence in the performances of social advisors as opposed to non-social advisors. A possible explanation might be that participants have a better insight into the abilities of social cues – typically other agents – than non-social cues – typically inanimate objects.

As the authors assumed simple Bayesian learning for the estimation of reliability in this study, the degree/speed of the learning should be examined with reference to the distance between the posterior and prior belief in the optimal Bayesian inference.

We thank the reviewer for this suggestion. We agree with the reviewer that further analyses that aim to disentangle the underlying mechanisms that might differ between both social and non-social conditions might provide additional theoretical contributions. We show additional model simulations and analyses that aim to disentangle the differences in more detail. These new results allowed clearer interpretations to be made.

In the current study, we showed that judgments made about non-social predictors were changed more strongly as a function of the subjective uncertainty: participants set a larger interval, indicating lower confidence, when they were more uncertain about the non-social cue’s accuracy to predict the target. In response to the reviewer’s comments, the new analyses were aimed at understanding under which conditions such a negative uncertainty effect might emerge.

Prior expectations of performance First, we compared whether participants had different prior expectations in the social condition compared to the non-social condition. One way to compare prior expectations is by comparing the first interval set for each advisor/predictor. This is a direct readout of the initial prior expectation with which participants approach our two conditions. In such a way, we test whether the prior beliefs before observing any social or non-social information differ between conditions. Even though this does not test the impact of prior expectations on subsequent belief updates, it does test whether participants have generally different expectations about the performance of social advisors or non-social predictors. There was no difference in this measure between social or non-social cues (Figure below; paired t-test social vs. non-social, t(23)= 0.01, p=0.98, 95% CI= [-0.067 0.68]).

Figure. Confidence interval for the first encounter of each predictor in social and non-social conditions. There was no initial bias in predicting the performance of social or non-social predictors.

Learning across time We have now seen that participants do not have an initial bias when predicting performances in social or non-social conditions. This suggests that differences between conditions might emerge across time when encountering predictors multiple times. We tested whether inherent differences in how beliefs are updated according to new observations might result in different impacts of uncertainty on interval setting between social and non-social conditions. More specifically, we tested whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. This approach was inspired by the reviewer’s comments about potential differences in the speed of learning as well as the reduction of uncertainty with increasing predictor encounters. Similar ideas were tested in previous studies, when comparing the learning rate (i.e. the speed of learning) in environments of different volatilities 12,13. In these studies, a smaller learning rate was prevalent in stable environments during which reward rates change slower over time, while higher learning rates often reflect learning in volatile environments so that recent observations have a stronger impact on behaviour. Even though most studies derived these learning rates with reinforcement learning models, similar ideas can be translated into a Bayesian model. For example, an established way of changing the speed of learning in a Bayesian model is to introduce noise during the update process14. This noise is equivalent to adding in some of the initial prior distribution and this will make the Bayesian updates more flexible to adapt to changing environments. It will widen the belief distribution and thereby make it more uncertain. Recent information has more weight on the belief update within a Bayesian model when beliefs are uncertain. This increases the speed of learning. In other words, a wide distribution (after adding noise) allows for quick integration of new information. On the contrary, a narrow distribution does not integrate new observations as strongly and instead relies more heavily on previous information; this corresponds to a small learning rate. So, we would expect a steep decline of uncertainty to be related to a smaller learning index while a slower decline of uncertainty is related to a larger learning index. We hypothesized that participants reduce their uncertainty quicker when observing social information, thereby anchoring more strongly on previous beliefs instead of integrating new observations flexibly. Vice versa, we hypothesized a less steep decline of uncertainty when observing non-social information, indicating that new information can be flexibly integrated during the belief update (new Figure 3a).

We modified the original Bayesian model (Figure 2d, Figure 2 – figure supplement 2) by adding a uniform distribution (equivalent to our prior distribution) to each belief update – we refer to this as noise addition to the Bayesian model14,21 . We varied the amount of noise between δ = [0,1], while δ= 0 equals the original Bayesian model and δ= 1 represents a very noisy Bayesian model. The uniform distribution was selected to match the first prior belief before any observation was made (equation 2). This δ range resulted in a continuous increase of subjective uncertainty around the belief about the angular error (Figure 3b-c). The modified posterior distribution denoted as 𝑝′(σ x) was derived at each trial as follows:

We applied each noisy Bayesian model to participants’ choices within the social and nonsocial condition.

The addition of a uniform distribution changed two key features of the belief distribution: first, the width of the distribution remains larger with additional observations, thereby making it possible to integrate new observations more flexibly. To show this more clearly, we extracted the model-derived uncertainty estimate across multiple encounters of the same predictor for the original model and the fully noisy Bayesian model (Figure 3 – figure supplement 1). The model-derived ‘uncertainty estimate’ of a noisy Bayesian model decays more slowly compared to the ‘uncertainty estimate’ of the original Bayesian model (upper panel). Second, the model-derived ‘accuracy estimate’ reflects more recent observations in a noisy Bayesian model compared to the ‘accuracy estimate’ derived from the original Bayesian model, which integrates past observations more strongly (lower panel). Hence, as mentioned beforehand, a rapid decay of uncertainty implies a small learning index; or in other words, stronger integration of past compared to recent observations.

In the following analyses, we tested whether an increasingly noisy Bayesian model mimics behaviour that is observed in the non-social compared to social condition. For example, we tested whether an increasingly noisy Bayesian model also exhibits a strongly negative ‘predictor uncertainty’ effect on interval setting (Figure 2e). In such a way, we can test whether differences in noise in the updating process of a Bayesian model might reproduce important qualitative differences in learning-related behaviour seen in the social and nonsocial conditions.

We used these modified Bayesian models to simulate trial-wise interval setting for each participant according to the observations they made when selecting a particular advisor or non-social cue. We simulated interval setting at each trial and examined whether an increase in noise produced model behaviours that resembled participant behaviour patterns observed in the non-social condition as opposed to social condition. At each trial, we used the accuracy estimate (Methods, equation 6) – which represents a subjective belief about a single angular error -- to derive an interval setting for the selected predictor. To do so, we first derived the point-estimate of the belief distribution at each trial (Methods, equation 6) and multiplied it with the size of one interval step on the circle. The step size was derived by dividing the circle size by the maximum number of possible steps. Here is an example of transforming an accuracy estimate into an interval: let’s assume the belief about the angular error at the current trial is 50 (Methods, equation 6). Now, we are trying to transform this number into an interval for the current predictor on a given trial. To obtain the size of one interval step, the circle size (360 degrees) is divided by the maximum number of interval steps (40 steps; note, 20 steps on each side), which results in nine degrees that represents the size of one interval step. Next, the accuracy estimate in radians (0,87) is multiplied by the step size in radians (0,1571) resulting in an interval of 0,137 radians or 7,85 degrees. The final interval size would be 7,85.

Simulating Bayesian choices in that way, we repeated the behavioural analyses (Figure 2b,e,f) to test whether intervals derived from more noisy Bayesian models mimic intervals set by participants in the non-social condition: greater changes in interval setting across trials (Figure 3 – figure supplement 1b), a negative ‘predictor uncertainty' effect on interval setting (Figure 3 – figure supplement 1c), and a higher learning index (Figure 3d).

First, we repeated the most crucial analysis -- the linear regression analysis (Figure 2e) and hypothesized that intervals that were simulated from noisy Bayesian models would also show a greater negative ‘predictor uncertainty’ effect on interval setting. This was indeed the case: irrespective of social or non-social conditions, the addition of noise (increased weighting of the uniform distribution in each belief update) led to an increasingly negative ‘predictor uncertainty’ effect on confidence judgment (new Figure 3d). In Figure 3d, we show the regression weights (y-axis) for the ‘predictor uncertainty’ on confidence judgment with increasing noise (x-axis). This result is highly consistent with the idea that that in the non-social condition the manner in which task estimates are updated is more uncertain and more noisy. By contrast, social estimates appear relatively more stable, also according to this new Bayesian simulation analysis.

This new finding extends the results and suggests a formal computational account of the behavioural differences between social and non-social conditions. Increasing the noise of the belief update mimics behaviour that is observed in the non-social condition: an increasingly negative effect of ‘predictor uncertainty’ on confidence judgment. Noteworthily, there was no difference in the impact that the noise had in the social and non-social conditions. This was expected because the Bayesian simulations are blind to the framing of the conditions. However, it means that the observed effects do not depend on the precise sequence of choices that participants made in these conditions. It therefore suggests that an increase in the Bayesian noise leads to an increasingly negative impact of ‘predictor uncertainty’ on confidence judgments irrespective of the condition. Hence, we can conclude that different degrees of uncertainty within the belief update is a reasonable explanation that can underlie the differences observed between social and non-social conditions.

Next, we used these simulated confidence intervals and repeated the descriptive behavioural analyses to test whether interval settings that were derived from more noisy Bayesian models mimic behavioural patterns observed in non-social compared to social conditions. For example, more noise in the belief update should lead to more flexible integration of new information and hence should potentially lead to a greater change of confidence judgments across predictor encounters (Figure 2b). Further, a greater reliance on recent information should lead to prediction errors more strongly in the next confidence judgment; hence, it should result in a higher learning index in the non-social condition that we hypothesize to be perceived as more uncertain (Figure 2f). We used the simulated confidence interval from Bayesian models on a continuum of noise integration (i.e. different weighting of the uniform distribution into the belief update) and derived again both absolute confidence change and learning indices (Figure 3 – figure supplement 1b-c).

‘Absolute confidence change’ and ‘learning index’ increase with increasing noise weight, thereby mimicking the difference between social and non-social conditions. Further, these analyses demonstrate the tight relationship between descriptive analyses and model-based analyses. They show that a noise in the Bayesian updating process is a conceptual explanation that can account for both the differences in learning and the difference in uncertainty processing that exist between social and non-social conditions. The key insight conveyed by the Bayesian simulations is that a wider, more uncertain belief distribution changes more quickly. Correspondingly, in the non-social condition, participants express more uncertainty in their confidence estimate when they set the interval, and they also change their beliefs more quickly as expressed in a higher learning index. Therefore, noisy Bayesian updating can account for key differences between social and non-social condition.

We thank the reviewer for making this point, as we believe that these additional analyses allow theoretical inferences to be made in a more direct manner; we think that it has significantly contributed towards a deeper understanding of the mechanisms involved in the social and non-social conditions. Further, it provides a novel account of how we make judgments when being presented with social and non-social information.

We made substantial changes to the main text, figures and supplementary material to include these changes:

Main text, page 10-11 new section:

The impact of noise in belief updating in social and non-social conditions

So far, we have shown that, in comparison to non-social predictors, participants changed their interval settings about social advisors less drastically across time, relied on observations made further in the past, and were less impacted by their subjective uncertainty when they did so (Figure 2). Using Bayesian simulation analyses, we investigated whether a common mechanism might underlie these behavioural differences. We tested whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. Similar ideas were tested in previous studies, when comparing the learning rate (i.e. the speed of learning) in environments of different volatilities12,13. We tested these ideas using established ways of changing the speed of learning during Bayesian updates14,21. We hypothesized that participants reduce their uncertainty quicker when observing social information. Vice versa, we hypothesized a less steep decline of uncertainty when observing non-social information, indicating that new information can be flexibly integrated during the belief update (Figure 5a).

We manipulated the amount of uncertainty in the Bayesian model by adding a uniform distribution to each belief update (Figure 3b-c) (equation 10,11). Consequently, the distribution’s width increases and is more strongly impacted by recent observations (see example in Figure 3 – figure supplement 1). We used these modified Bayesian models to simulate trial-wise interval setting for each participant according to the observations they made by selecting a particular advisor in the social condition or other predictor in the nonsocial condition. We simulated confidence intervals at each trial. We then used these to examine whether an increase in noise led to simulation behaviour that resembled behavioural patterns observed in non-social conditions that were different to behavioural patterns observed in the social condition.

First, we repeated the linear regression analysis and hypothesized that interval settings that were simulated from noisy Bayesian models would also show a greater negative ‘predictor uncertainty’ effect on interval setting resembling the effect we had observed in the nonsocial condition (Figure 2e). This was indeed the case when using the noisy Bayesian model: irrespective of social or non-social condition, the addition of noise (increasing weight of the uniform distribution to each belief update) led to an increasingly negative ‘predictor uncertainty’ effect on confidence judgment (new Figure 3d). The absence of difference between the social and non-social conditions in the simulations, suggests that an increase in the Bayesian noise is sufficient to induce a negative impact of ‘predictor uncertainty’ on interval setting. Hence, we can conclude that different degrees of noise in the updating process are sufficient to cause differences observed between social and non-social conditions. Next, we used these simulated interval settings and repeated the descriptive behavioural analyses (Figure 2b,f). An increase in noise led to greater changes of confidence across time and a higher learning index (Figure 3 – figure supplement 1b-c). In summary, the Bayesian simulations offer a conceptual explanation that can account for both the differences in learning and the difference in uncertainty processing that exist between social and non-social conditions. The key insight conveyed by the Bayesian simulations is that a wider, more uncertain belief distribution changes more quickly. Correspondingly, in the non-social condition, participants express more uncertainty in their confidence estimate when they set the interval, and they also change their beliefs more quickly. Therefore, noisy Bayesian updating can account for key differences between social and non-social condition.

Methods, page 23 new section:

Extension of Bayesian model with varying amounts of noise

We modified the original Bayesian model (Figure 2d, Figure 2 – figure supplement 2) to test whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. [...] To obtain the size of one interval step, the circle size (360 degrees) is divided by the maximum number of interval steps (40 steps; note, 20 steps on each side), which results in nine degrees that represents the size of one interval step. Next, the accuracy estimate in radians (0,87) is multiplied by the step size in radians (0,1571) resulting in an interval of 0,137 radians or 7,85 degrees. The final interval size would be 7,85.

We repeated behavioural analyses (Figure 2b,e,f) to test whether confidence intervals derived from more noisy Bayesian models mimic behavioural patterns observed in the nonsocial condition: greater changes of confidence across trials (Figure 3 – figure supplement 1b), a greater negative ‘predictor uncertainty' on confidence judgment (Figure 3 – figure supplement 1c) and a greater learning index (Figure 3d).

Discussion, page 14: […] It may be because we make just such assumptions that past observations are used to predict performance levels that people are likely to exhibit next 15,16. An alternative explanation might be that participants experience a steeper decline of subjective uncertainty in their beliefs about the accuracy of social advice, resulting in a narrower prior distribution, during the next encounter with the same advisor. We used a series of simulations to investigate how uncertainty about beliefs changed from trial to trial and showed that belief updates about non-social cues were consistent with a noisier update process that diminished the impact of experiences over the longer term. From a Bayesian perspective, greater certainty about the value of advice means that contradictory evidence will need to be stronger to alter one’s beliefs. In the absence of such evidence, a Bayesian agent is more likely to repeat previous judgments. Just as in a confirmation bias 17, such a perspective suggests that once we are more certain about others’ features, for example, their character traits, we are less likely to change our opinions about them.

Reviewer #2 (Public Review):

Humans learn about the world both directly, by interacting with it, and indirectly, by gathering information from others. There has been a longstanding debate about the extent to which social learning relies on specialized mechanisms that are distinct from those that support learning through direct interaction with the environment. In this work, the authors approach this question using an elegant within-subjects design that enables direct comparisons between how participants use information from social and non-social sources. Although the information presented in both conditions had the same underlying structure, participants tracked the performance of the social cue more accurately and changed their estimates less as a function of prediction error. Further, univariate activity in two regions-dmPFC and pTPJ-tracked participants' confidence judgments more closely in the social than in the non-social condition, and multivariate patterns of activation in these regions contained information about the identity of the social cues.

Overall, the experimental approach and model used in this paper are very promising. However, after reading the paper, I found myself wanting additional insight into what these condition differences mean, and how to place this work in the context of prior literature on this debate. In addition, some additional analyses would be useful to support the key claims of the paper.

We thank the reviewer for their very supportive comments. We have addressed their points below and have highlighted changes in our manuscript that we made in response to the reviewer’s comments.

(1) The framing should be reworked to place this work in the context of prior computational work on social learning. Some potentially relevant examples:

• Shafto, Goodman & Frank (2012) provide a computational account of the domainspecific inductive biases that support social learning. In brief, what makes social learning special is that we have an intuitive theory of how other people's unobservable mental states lead to their observable actions, and we use this intuitive theory to actively interpret social information. (There is also a wealth of behavioral evidence in children to support this account; for a review, see Gweon, 2021).

• Heyes (2012) provides a leaner account, arguing that social and non-social learning are supported by a common associative learning mechanism, and what distinguishes social from non-social learning is the input mechanism. Social learning becomes distinctively "social" to the extent that organisms are biased or attuned to social information.

I highlight these papers because they go a step beyond asking whether there is any difference between mechanisms that support social and nonsocial learning-they also provide concrete proposals about what that difference might be, and what might be shared. I would like to see this work move in a similar direction.

References<br /> (In the interest of transparency: I am not an author on these papers.)

Gweon, H. (2021). Inferential social learning: how humans learn from others and help others learn. PsyArXiv. https://doi.org/10.31234/osf.io/8n34t

Heyes, C. (2012). What's social about social learning?. Journal of Comparative Psychology, 126(2), 193.

Shafto, P., Goodman, N. D., & Frank, M. C. (2012). Learning from others: The consequences of psychological reasoning for human learning. Perspectives on Psychological Science, 7(4), 341-351.

Thank you for this suggestion to expand our framing. We have now made substantial changes to the Discussion and Introduction to include additional background literature, the relevant references suggested by the reviewer, addressing the differences between social and non-social learning. We further related our findings to other discussions in the literature that argue that differences between social and non-social learning might occur at the level of algorithms (the computations involved in social and non-social learning) and/or implementation (the neural mechanisms). Here, we describe behaviour with the same algorithm (Bayesian model), but the weighing of uncertainty on decision-making differs between social and non-social contexts. This might be explained by similar ideas put forward by Shafto and colleagues (2012), who suggest that differences between social and non-social learning might be due to the attribution of goal-directed intention to social agents, but not non-social cues. Such an attribution might lead participants to assume that advisor performances will be relatively stable under the assumption that they should have relatively stable goal-directed intentions. We also show differences at the implementational level in social and non-social learning in TPJ and dmPFC.

Below we list the changes we have made to the Introduction and Discussion. Further, we would also like to emphasize the substantial extension of the Bayesian modelling which we think clarifies the theoretical framework used to explain the mechanisms involved in social and non-social learning (see our answer to the next comments below).

Introduction, page 4:

[...]<br /> Therefore, by comparing information sampling from social versus non-social sources, we address a long-standing question in cognitive neuroscience, the degree to which any neural process is specialized for, or particularly linked to, social as opposed to non-social cognition 2–9. Given their similarities, it is expected that both types of learning will depend on common neural mechanisms. However, given the importance and ubiquity of social learning, it may also be that the neural mechanisms that support learning from social advice are at least partially specialized and distinct from those concerned with learning that is guided by nonsocial sources.

However, it is less clear on which level information is processed differently when it has a social or non-social origin. It has recently been argued that differences between social and non-social learning can be investigated on different levels of Marr’s information processing theory: differences could emerge at an input level (in terms of the stimuli that might drive social and non-social learning), at an algorithmic level or at a neural implementation level 7. It might be that, at the algorithmic level, associative learning mechanisms are similar across social and non-social learning 1. Other theories have argued that differences might emerge because goal-directed actions are attributed to social agents which allows for very different inferences to be made about hidden traits or beliefs 10. Such inferences might fundamentally alter learning about social agents compared to non-social cues.

Discussion, page 15:

[…] One potential explanation for the assumption of stable performance for social but not non-social predictors might be that participants attribute intentions and motivations to social agents. Even if the social and non-social evidence are the same, the belief that a social actor might have a goal may affect the inferences made from the same piece of information 10. Social advisors first learnt about the target’s distribution and accordingly gave advice on where to find the target. If the social agents are credited with goal-directed behaviour then it might be assumed that the goals remain relatively constant; this might lead participants to assume stability in the performances of social advisors. However, such goal-directed intentions might not be attributed to non-social cues, thereby making judgments inherently more uncertain and changeable across time. Such an account, focussing on differences in attribution in social settings aligns with a recent suggestion that any attempt to identify similarities or differences between social and non-social processes can occur at any one of a number of the levels in Marr’s information theory 7. Here we found that the same algorithm was able to explain social and non-social learning (a qualitatively similar computational model could explain both). However, the extent to which the algorithm was recruited when learning about social compared to non-social information differed. We observed a greater impact of uncertainty on judgments about social compared to non-social information. We have shown evidence for a degree of specialization when assessing social advisors as opposed to non-social cues. At the neural level we focused on two brain areas, dmPFC and pTPJ, that have not only been shown to carry signals associated with belief inferences about others but, in addition, recent combined fMRI-TMS studies have demonstrated the causal importance of these activity patterns for the inference process […]

(2) The results imply that dmPFC and pTPJ differentiate between learning from social and non-social sources. However, more work needs to be done to rule out simpler, deflationary accounts. In particular, the condition differences observed in dmPFC and pTPJ might reflect low-level differences between the two conditions. For example, the social task could simply have been more engaging to participants, or the social predictors may have been more visually distinct from one another than the fruits.

We understand the reviewer’s concern regarding low-level distinctions between the social and non-social condition that could confound for the differences in neural activation that are observed between conditions in areas pTPJ and dmPFC. From the reviewer’s comments, we understand that there might be two potential confounders: first, low-level differences such that stimuli within one condition might be more distinct to each other compared to the relative distinctiveness between stimuli within the other condition. Therefore, simply the greater visual distinctiveness of stimuli in one condition than another might lead to learning differences between conditions. Second, stimuli in one condition might be more engaging and potentially lead to attentional differences between conditions. We used a combination of univariate analyses and multivariate analyses to address both concerns.

Analysis 1: Univariate analysis to inspect potential unaccounted variance between social and non-social condition

First, we used the existing univariate analysis (exploratory MRI whole-brain analysis, see Methods) to test for neural activation that covaried with attentional differences – or any other unaccounted neural difference -- between conditions. If there were neural differences between conditions that we are currently not accounting for with the parametric regressors that are included in the fMRI-GLM, then these differences should be captured in the constant of the GLM model. For example, if there are attentional differences between conditions, then we could expect to see neural differences between conditions in areas such as inferior parietal lobe (or other related areas that are commonly engaged during attentional processes).

Importantly, inspection of the constant of the GLM model should capture any unaccounted differences, whether they are due to attention or alternative processes that might differ between conditions. When inspecting cluster-corrected differences in the constant of the fMRI-GLM model during the setting of the confidence judgment, there were no clustersignificant activation that was different between social and non-social conditions (Figure 4 – figure supplement 4a; results were familywise-error cluster-corrected at p<0.05 using a cluster-defining threshold of z>2.3). For transparency, we show the sub-threshold activation map across the whole brain (z > 2) for the ‘constant’ contrasted between social and nonsocial condition (i.e. constant, contrast: social – non-social).

For transparency we additionally used an ROI-approach to test differences in activation patterns that correlated with the constant during the confidence phase – this means, we used the same ROI-approach as we did in the paper to avoid any biased test selection. We compared activation patterns between social and non-social conditions in the same ROI as used before; dmPFC (MNI-coordinate [x/y/z: 2,44,36] 16), bilateral pTPJ (70% probability anatomical mask; for reference see manuscript, page 23) and additionally compared activation patterns between conditions in bilateral IPLD (50% probability anatomical mask, 20). We did not find significantly different activation patterns between social and non-social conditions in any of these areas: dmPFC (confidence constant; paired t-test social vs nonsocial: t(23) = 0.06, p=0.96, [-36.7, 38.75]), bilateral TPJ (confidence constant; paired t-test social vs non-social: t(23) = -0.06, p=0.95, [-31, 29]), bilateral IPLD (confidence constant; paired t-test social vs non-social: t(23) = -0.58, p=0.57, [-30.3 17.1]).

There were no meaningful activation patterns that differed between conditions in either areas commonly linked to attention (eg IPL) or in brain areas that were the focus of the study (dmPFC and pTPJ). Activation in dmPFC and pTPJ covaried with parametric effects such as the confidence that was set at the current and previous trial, and did not correlate with low-level differences such as attention. Hence, these results suggest that activation between conditions was captured better by parametric regressors such as the trial-wise interval setting, i.e. confidence, and are unlikely to be confounded by low-level processes that can be captured with univariate neural analyses.

Analysis 2: RSA to test visual distinctiveness between social and non-social conditions

We addressed the reviewer’s other comment further directly by testing whether potential differences between conditions might arise due to a varying degree of visual distinctiveness in one stimulus set compared to the other stimulus set. We used RSA analysis to inspect potential differences in early visual processes that should be impacted by greater stimulus similarity within one condition. In other words, we tested whether the visual distinctiveness of one stimuli set was different to the visual distinctiveness of the other stimuli set. We used RSA analysis to compare the Exemplar Discriminability Index (EDI) between conditions in early visual areas. We compared the dissimilarity of neural activation related to the presentation of an identical stimulus across trials (diagonal in RSA matrix) with the dissimilarity in neural activation between different stimuli across trials (off-diagonal in RSA matrix). If stimuli within one stimulus set are very similar, then the difference between the diagonal and off-diagonal should be very small and less likely to be significant (i.e. similar diagonal and off-diagonal values). In contrast, if stimuli within one set are very distinct from each other, then the difference between the diagonal and off-diagonal should be large and likely to result in a significant EDI (i.e. different diagonal and off-diagonal values) (see Figure 4g for schematic illustration). Hence, if there is a difference in the visual distinctiveness between social and non-social conditions, then this difference should result in different EDI values for both conditions – hence, visual distinctiveness between the stimuli set can be tested by comparing the EDI values between conditions within the early visual processing. We used a Harvard-cortical ROI mask based on bilateral V1. Negative EDI values indicate that the same exemplars are represented more similarly in the neural V1 pattern than different exemplars. This analysis showed that there was no significant difference in EDI between conditions (Figure 4 – figure supplement 4b; EDI paired sample t-test: t(23) = -0.16, p=0.87, 95% CI [-6.7 5.7]).

We have further replicated results in V1 with a whole-brain searchlight analysis, averaging across both social and non-social conditions.

In summary, by using a combination of univariate and multivariate analyses, we could test whether neural activation might be different when participants were presented with a facial or fruit stimuli and whether these differences might confound observed learning differences between conditions. We did not find meaningful neural differences that were not accounted for with the regressors included in the GLM. Further, we did not find differences in the visual distinctiveness between the stimuli sets. Hence, these control analyses suggest that differences between social and non-social conditions might not arise because of differences in low-level processes but are instead more likely to develop when learning about social or non-social information.

Moreover, we also examined behaviourally whether participants differed in the way they approached social and non-social condition. We tested whether there were initial biases prior to learning, i.e. before actually receiving information from either social or non-social information sources. Therefore, we tested whether participants have different prior expecations about the performance of social compared to non-social predictors. We compared the confidence judgments at the first trial of each predictor. We found that participants set confidence intervals very similarly in social and non-social conditions (Figure below). Hence, it did not seem to be the case that differences between conditions arose due to low level differences in stimulus sets or prior differences in expectations about performances of social compared to non-social predictors. However, we can show that differences between conditions are apparent when updating one’s belief about social advisors or non-social cues and as a consequence, in the way that confidence judgments are set across time.

Figure. Confidence interval for the first encounter of each predictor in social and non-social conditions. There was no initial bias in predicting the performance of social or non-social predictors.

Main text page 13:

[… ]<br /> Additional control analyses show that neural differences between social and non-social conditions were not due to the visually different set of stimuli used in the experiment but instead represent fundamental differences in processing social compared to non-social information (Figure 4 – figure supplement 4). These results are shown in ROI-based RSA analysis and in whole-brain searchlight analysis. In summary, in conjunction, the univariate and multivariate analyses demonstrate that dmPFC and pTPJ represent beliefs about social advisors that develop over a longer timescale and encode the identities of the social advisors.

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Author Response

Reviewer #2 (Public Review):

1) Although the images and videos were of great quality, the results derived from them provided little new knowledge and few conceptual insights into male reproductive tract biology and basically confirmed what has been published using traditional methods. For example, the high intensity of the vascular network in the initial segment was previously reported by Abe in 1984 and Suzuki in 1982; the pattern of the major lymphatic vessel and drainage was beautifully depicted by Perez-Clavier, 1982.

We thank the reviewer for his/her appreciative comments regarding the quality of the images/videos we provide in this study. We do not fully agree with his/her assessment of the lack of novelty. Our work confirms earlier reports that are now dated (1980s), which in itself is worth mentioning for the interested community, especially when the confirmation uses the most advanced technologies available today. We have never said that nothing was done in the past, and we have acknowledged all past contributors (including those mentioned by the reviewer) by pointing out the limitations of the technical tools that were available at the time. In addition, our current work provides a more comprehensive and global view by extending our approach to the entire mouse epididymis, whereas previous work was much more limited.

2) The authors were very cautious when interpreting the results of marker immunostaining however these markers were not specific for a definite cell type. For example, as the authors stated, VEGFR3 marks both lymphatic vessels and fenestrated blood vessels. how could the authors claim the VEGFR3+ network was lymphatic? The authors claimed that they used three markers for the lymphatic vessel. But staining results of the networks were very different. How could the author make conclusions about the network of lymphatic vessels in the epididymis?

We broadly agree with the reviewer and have made it clear that one cannot be 100% sure that all the VEGFR3+ structures we present are lymphatic. However, in total, we used 4 documented lymphatic markers (not 3 as mentioned by the reviewer) which are (VEGFR3, LYVE1, PROX1 and PDPN). Three of them give very similar profiles, while only PDPN shows some differences. We are currently studying in more detail the expression of PDPN in the mouse epididymis because we speculate that this marker may target a population of pluripotent cells in this tissue. Therefore, with the 3 similar profiles and with the subtraction of PVLAP+ structures, we are pretty confident that what we show corresponds to the different lymphatic structures.

3) To understand the vascular network development in the epididymis, would the authors please look at the fetal stage when the vascular network is established in the first place? Wolffian duct tissues are much smaller and thinner and would be amenable for 3D imaging probably even without clearing.

We generally agree with the reviewer that this could be an interesting addition. However, it represents a significant amount of additional work. Organ clearing will certainly be required because it is unlikely that Wolffian duct will be sufficiently transparent to allow lightsheet microscopy. In the literature, the study of Wolffian duct relies primarily on whole mounts, inclusions, and cryosections. Besides the fact that this represents a lot of extra work, we are not totally convinced that this would be of much use. A key reason is that the epididymis is an organ that differentiates completely after birth (Robaire and Hinton, 2015). It is reported that differentiation of mouse caput segment 1 occurs around 19DPN (Xu et al., 2016) and is intimately related to the development of the vasculature (Lebarr et al., 1986). Regarding the lymphatic network, Swingen et al, (2012) reports that lymphangiogenesis in the mouse testis and epididymis is initiated late in gestation after 15DPC. Videos showing the external lymphatic vessels of the testis and epididymis at 17.5DPC can be seen at https://doi.org/10.1371/journal.pone.0052620.s002. The authors indicate that lymphangiogenesis occurs via sprouting from the adjacent mesonephros. We hypothesize that the more internal lymphatics evolve between birth and 10DPN, which corresponds to the time when we observed LEPC Lyve1pos cells.

4) Immunofluorescence staining of VEGF factors was not convincing. As a secreted factor, VEGF will be secreted out of the cells, would it be detected more in the interstitium? I am always skeptical about the results of immunostaining secreted growth factors. Would it be possible to perform in situ or RNAscope to confirm the spatial expression pattern of VEGFs?

Well, active VEGF factors result from alternative mRNA splicing events and posttranslational proteolytic cleavage. Therefore, in our opinion, the study of VEGF mRNA by in situ hybridization or RNAscope analysis will not be very informative about the actual presence of active forms of VEGF in the epididymis. If necessary, we can provide as supplementary material immunohistochemistry data showing the presence of VEFG-A in the epididymal principal cells. Our major objective with these data was to show that VEGF factors and their respective receptors were present in the epididymis. Nevertheless, in an attempt to convince the reviewer, we provide as accompanying data to this rebuttal letter new sets of figures (Figures VEGF-A-response editor & VEGFC /VEGF-D-response editor) that we believe can improve the perception of our data. If the editorial office feels it is necessary, these figures could be added to the supplementary figure set (as Figure 6figure supplement 1 and Figure 6-figure supplement 2). For VEGF-A the data exists already in the literature as we have indicated (Korpelainen, 1998). In fine, our goal was not to show which cell types of the epididymis epithelium produce VEGFs but rather than VEGF factors and their receptors where there in order to support angiogenesis or lymphangiogenic activity in the tissue. In addition, we hypothesize that because septa have been reported to constitute barriers between segments restricting passive diffusion of molecules (Turner et al., 2003; Stammler et al., 2015), the VEGF factors are expected to be produced locally.

Figure VEGF-A - response editor : Immunofluorescence of the angiogenic ligand VEGF-A in the epididymis. Figure 6 shows that this ligand is mainly found in the caput and more precisely in S1.It is very strongly expressed in the peritubular microvascularization of the SI which expresses the VEGFR3:YFP transgene whereas it is less expressed by intertubular blood vessels (asterisk). This seems to indicate that it is the peritubular vessels that are in the majority responsible for the angiogenic activity measured in our study. Furthermore, it is expressed by the epithelium as secretory vesicles (IS, and S3 and enlargement) which is in agreement with in situ hybridization work performed by Korpelainene E.I et al J.Cell.biol 1998). The enlargement shown in S3_Z shows the sagital plane of the tubule where one can distinguish VEGFR:YFP positive cells that strongly express are also VEGF-A positive indicating that the same cells of the epithelium express both the receptor and the ligand. Here the transgene is detected directly without the use of an anti-GFP which allows to enhance the signal.

Figure VEGF-C / VEGF-D - response editor : Immunofluorescence of VEGF-C and VEGF-D lymphangiogenic ligands in the epididymis. This figure shows that these ligands are mainly found in the interstitial tissue throughout the organ with a higher proportion in the caudal part. This expression may be largely driven by fibroblasts, which are widely represented in the interstitium, or by endothelial cells, since these two ligands are expressed by these cell types. However, as shown in the figures and in the enlargement of panel A, VEGF-C is also produced by epithelial cells within what may appear as secretory vesicles. In contrast, for VEGF-D, we observe only few weakly positive epithelial cells (panel B). These ligands are also detected in the lumen of epididymal tubules (visible for VEGF-C Panel A S2). This presence may be explained by lumicrine transfer from the testis, in addition to secretion from epithelial cells. Here the transgene is detected directly without the use of an anti-GFP which allows to enhance the signal.

5) The study is descriptive and does not provide functional and mechanistic insights. Maybe, the combination of 3D imaging with lineage tracing of endothelium cells or ligation study (removal/ligation of the certain vessel) would help better understand how the vascular network is established and their functional significance.

The technical approaches suggested by the reviewer could certainly improve our understanding of the rather complex epididymal vascular network. Taken together, they represent the body of a comprehensive follow-up study that is worth undertaking.

6) Immune response is among many physiological processes in which vascular networks play significant roles. Discussion would be needed in other physiological processes, such as tissue metabolism and stem/progenitor cell niche microenvironment.

We agree with the reviewer that the mammalian vasculature is involved in other physiological processes beyond immune/inflammatory responses. We have deliberately chosen to focus our discussion on the inflammatory and immune context of the epididymis, as we believe this is the most relevant aspect. It is also in full agreement with the research that our team has been conducting for 15 years to try to understand the complex orchestration of tolerance versus immune surveillance in this territory. This is a finely tuned process that, if properly understood, can help to understand and appropriately treat clinical situations of infertility and/or urological problems. As our discussion section is already quite long, we feel that it was not justified to extend it further on other aspects. However, in response to the reviewer's suggestion, we now mention at the end of the first paragraph of the discussion that the epididymal vascular network is likely to serve different processes in this tissue (page 9, lines 299 to 303).

7) How could the author determine the Cd-A labeled vessel in Fig 1 was an artery, not a vein? This leads to another critical question. Would it be possible to stain with artery and vein markers to help illustrate the blood flow directions of the vessel?

The reviewer is right on the fact that we arbitrarily called the Cd-A vessel in Figure 1 an artery. Cd-A is not an acronym we use anymore. What we have done is to use the acronym SEA (superior epididymal artery) to indicate what we firmly believe to be an artery, as also suggested by previous literature (e.g., Suzuki, 1982; Abe et al, 1982) in which this same structure has been consistently referred to as an artery. For other blood vessels, we now have used the acronym "Cd-BV" because we do not know whether we are dealing with a vein or an artery as rightfully pointed out by the reviewer. This is clearly stated in the legend of Figure 1.

Author Response

Reviewer #1 (Public Review):

The authors ask an interesting question as to whether working memory contains more than one conjunctive representation of multiple task features required for a future response with one of these representations being more likely to become relevant at the time of the response. With RSA the authors use a multivariate approach that seems to become the standard in modern EEG research.

We appreciate the reviewer’s helpful comments on the manuscript and their encouraging comments regarding its potential impact.

I have three major concerns that are currently limiting the meaningfulness of the manuscript: For one, the paradigm uses stimuli with properties that could potentially influence involuntary attention and interfere in a Stroop-like manner with the required responses (i.e., 2 out of 3 cues involve the terms "horizontal" or "vertical" while the stimuli contain horizontal and vertical bars). It is not clear to me whether these potential interactions might bring about what is identified as conjunctive representations or whether they cause these representations to be quite weak.

We agree it is important to rule out any effects of involuntary attention that might have been elicited by our stimulus choices. To address the Reviewer’s concern, we conducted control analyses to test if there was any influence of Stroop-like interference on our measures of behavior or the conjunctive representation. To summarize these analyses (detailed in our responses below and in the supplemental materials), we found no evidence of the effect of compatibility on behavior or on the decoding of conjunctions during either the maintenance or test periods. Furthermore, we found that the decoding of the bar orientation was at chance level during the interval when we observe evidence of the conjunctive representations. Thus, we conclude that the compatibility of the stimuli and the rule did not contribute to the decoding of conjunctive representations or to behavior.

Second, the relatively weak conjunctive representations are making it difficult to interpret null effects such as the absence of certain correlations.

The reviewer is correct that we cannot draw strong conclusions from null findings. We have revised the main text accordingly. In certain cases, we have also included additional analyses. These revisions are described in detail in response the reviewer’s comments below.

Third, if the conjunctive representations truly are reflections of working memory activity, then it would help to include a control condition where memory load is reduced so as to demonstrate that representational strength varies as a function of load. Depending on whether these concerns or some of them can be addressed or ruled out this manuscript has the potential of becoming influential in the field.

This is a clever suggestion for further experimentation. We agree that observing the adverse effect of memory load is one of the robust ways to assess the contributions of working memory system for future studies. However, given that decoding is noisy during the maintenance period (particularly for the low-priority conjunctive representation) even with a relatively low set-size, we expect that in order to further manipulate load, we would need to alter the research design substantially. Thus, as the main goal of the current study is to study prioritization and post-encoding selection of action-related information, we focused on the minimum set-size required for this question (i.e., load 2). However, we now note this load manipulation as a direction for future research in the discussion (pg. 18).

Reviewer #2 (Public Review):

Kikumoto and colleagues investigate the way visual-motor representations are stored in working memory and selected for action based on a retro-cue. They make use of a combination of decoding and RSA to assess at which stages of processing sensory, motor, and conjunctive information (consisting of sensory and motor representations linked via an S- R mapping) are represented in working memory and how these mental representations are related to behavioral performance.

Strengths

This is an elaborate and carefully designed experiment. The authors are able to shed further light on the type of mental representations in working memory that serve as the basis for the selection of relevant information in support of goal- directed actions. This is highly relevant for a better understanding of the role of selective attention and prospective motor representations in working memory. The methods used could provide a good basis for further research in this regard.

We appreciate these helpful comments and the Reviewer’s positive comments on the impact of the work.

Weaknesses

There are important points requiring further clarification, especially regarding the statistical approach and interpretation of results.

• Why is there a conjunction RSA model vector (b4) required, when all information for a response can be achieved by combining the individual stimulus, response, and rule vectors? In Figure 3 it becomes obvious that the conjunction RSA scores do not simply reflect the overlap of the other three vectors. I think it would help the interpretation of results to clearly state why this is not the case.

Thank you for the suggestion, we’ve now added the theoretical background that motivates us to include the RSA model of conjunctive representation (pg. 4 and 5). In particular, several theories of cognitive control have proposed that over the course of action planning, the system assembles an event (task) file which binds all task features at all levels – including the rule (i.e., context), stimulus, and response – into an integrated, conjunctive representation that is essential for an action to be executed (Hommel 2019; Frings et al. 2020). Similarly, neural evidence of non-human primates suggests that cognitive tasks that require context-dependency (e.g., flexible remapping of inputs to different outputs based on the context) recruit nonlinear conjunctive representations (Rigotti et al. 2013; Parthasarathy et al. 2019; Bernardi et al. 2020; Panichello and Buschman, 2021). Supporting these views, we previously observed that conjunctive representations emerge in the human brain during action selection, which uniquely explained behavior such as the costs in transition of actions (Kikumoto & Mayr, 2020; see also Rangel & Hazeltine & Wessel, 2022) or the successful cancelation of actions (Kikumoto & Mayr, 2022). In the current study, by using the same set of RSA models, we attempted to extend the role of conjunctive representations for planning and prioritization of future actions. As in the previous studies (and as noted by the reviewer), the conjunction model makes a unique prediction of the similarity (or dissimilarity) pattern of the decoder outputs: a specific instance of action that is distinct from others actions. This contrasts to other RSA models of low-level features that predict similar patterns of activities for instances that share the same feature (e.g., S-R mappings 1 to 4 share the diagonal rule context). Here, we generally replicate the previous studies showing the unique trajectories of conjunctive representations (Figure 3) and their unique contribution on behavior (Figure 5).

• One of the key findings of this study is the reliable representation of the conjunction information during the preparation phase while there is no comparable effect evident for response representations. This might suggest that two potentially independent conjunctive representations can be activated in working memory and thereby function as the basis for later response selection during the test phase. However, the assumption of the independence of the high and low priority conjunction representations relies only on the observation that there was no statistically reliable correlation between the high and low priority conjunctions in the preparation and test phases. This assumption is not valid because non-significant correlations do not allow any conclusion about the independence of the two processes. A comparable problem appeared regarding the non-significant difference between high and low-priority representations. These results show that it was not possible to prove a difference between these representations prior to the test phase based on the current approach, but they do not unequivocally "suggest that neither action plan was selectively prioritized".

We appreciate this important point. We have taken care in the revision to state that we find evidence of an interference effect for the high-priority action and do not find evidence for such an effect from the low-priority action. Thus, we do not intend to conclude that no such effect could exist. Further, although it is not our intention to draw a strong conclusion from the null effect (i.e., no correlations), we performed an exploratory analysis where we tested the correlation in trials where we observed strong evidence of both conjunctions. Specifically, we binned trials into half within each time point and individual subject and performed the multi-level model analysis using trials where both high and low priority conjunctions were above their medians. Thus, we selected trials in such a way that they are independent of the effect we are testing. The figure below shows the coefficient of associated with low-priority conjunction predicting high-priority conjunction (uncorrected). Even when we focus on trials where both conjunctions are detected (i.e., a high signal-to-noise ratio), we observed no tradeoff. Again, we cannot draw strong conclusions based on the null result of this exploratory analysis. Yet, we can rule out some causes of no correlation between high and low priority conjunctions such as the poor signal-to-noise ratio of the low priority conjunctions. We have further clarified this point in the result (pg. 14).

Fig. 1. Trial-to-trial variability between high and low priority conjunctions, using above median trials. The coefficients of the multilevel regression model predicting the variability in trial-to-trial highpriority conjunction by low-priority conjunction.

• The experimental design used does not allow for a clear statement about whether pure motor representations in working memory only emerge with the definition of the response to be executed (test phase). It is not evident from Figure 3 that the increase in the RSA scores strictly follows the onset of the Go stimulus. It is also conceivable that the emergence of a pure motor representation requires a longer processing time. This could only be investigated through temporally varying preparation phases.

We agree with the reviewer. Although we detected no evidence of response representations of both high and low priority action plans during the preparation phase, t(1,23) = -.514, beta = .002, 95% CI [-.010 .006] for high priority; t(1,23) = -1.57, beta = -.008, 95% CI [-.017 .002] for low priority, this may be limited by the relatively short duration of the delay period (750 ms) in this study. However, in our previous studies using a similar paradigm without a delay period (Kikumoto & Mayr, 2020; Kikumoto & Mayr, 2022), response representations were detected less than 300ms after the response was specified, which corresponds to the onset of delay period in this study. Further, participants in the current study were encouraged to prepare responses as early as possible, using adaptive response deadlines and performance-based incentives. Thus, we know of no reason why responses would take longer to prepare in the present study. But we agree that we can’t rule this out. We have added the caveat noted above, as well as this additional context in the discussion (pg. 16-17).

• Inconsistency of statistical approaches: In the methods section, the authors state that they used a cluster-forming threshold and a cluster-significance threshold of p < 0.05. In the results section (Figure 4) a cluster p-value of 0.01 is introduced. Although this concerns different analyses, varying threshold values appear as if they were chosen in favor of significant results. The authors should either proceed consistently here or give very good reasons for varying thresholds.

We thank the reviewer for noting this oversight. All reported significant clusters with cluster P-value were identified using a cluster-forming threshold, p < .05. We fixed the description accordingly.

• Interpretation of results: The significant time window for the high vs. low priority by test-type interaction appeared quite late for the conjunction representation. First, it does not seem reasonable that such an effect appears in a time window overlapping with the motor responses. But more importantly, why should it appear after the respective interaction for the response representation? When keeping in mind that these results are based on a combination of time-frequency analysis, decoding, and RSA (quite many processing steps), I find it hard to really see a consistent pattern in these results that allows for a conclusion about how higher-level conjunctive and motor representations are selected in working memory.

Thank you for raising this important point. First, we fixed reported methodological inconsistencies such as the cluster P-value and cluster-forming threshold). Further, we fully agree that the difference in the time course for the response and conjunctive representations in the low priority, tested condition is unexpected and would complicate the perspective that the conjunctive representation contributes to efficient response selection. However, additional analysis indicates that this apparent pattern in the stimulus locked result is misleading and there is a more parsimonious explanation. First, we wish to caution that the data are relatively noisy and likely are influenced by different frequency bands for different features. Thus, fine-grained temporal differences should be interpreted with caution in the absence of positive statistical evidence of an interaction over time. Indeed, though Figure 4 in the original submission shows a quantitative difference in timing of the interaction effect (priority by test type) across conjunctive representation and response representation, the direct test of this four way interaction [priority x test type x representation type (conjunction vs. response), x time interval (1500 ms to 1850 ms vs. 1850 to 2100 ms)] is not significant, t(1,23) = 1.65, beta = .058, 95% CI [-.012 .015]). The same analysis using response-aligned data is also not significant, t(1,23) = -1.24, beta = -.046, 95% CI [-.128 .028]). These observations were not dependent on the choice of time interval, as other time intervals were also not significant. Therefore, we do not have strong evidence that this is a true timing difference between these conditions and believe this is likely driven by noise.

Further, we believe the apparent late emergence of difference in two conjunctions when the low priority action is tested is more likely due to a slow decline in the strength of the untested high priority conjunction rather than a late emergence of the low priority conjunction. This pattern is clearer when the traces are aligned to the response. The tested low priority conjunction emerges early and is sustained when it is the tested action and declines when it is untested (-226 ms to 86 ms relative to the response onset, cluster-forming threshold, p < .05). These changes eventually resulted in a significant difference in strength between the tested versus untested low priority conjunctions just prior to the commission of the response (Figure 4 - figure supplement 1, the panel on right column of the middle row, the black bars at the top of panel). Importantly, the high priority conjunction also remains active in its untested condition and declines later than the untested low priority conjunction does. Indeed, the untested high priority conjunction does not decline significantly relative to trials when it is tested until after the response is emitted (Figure 4 - figure supplement 1, the panel on right column of the middle row, the red bars at the top of panel). This results in a late emerging interaction effect of the priority and test type, but this is not due to a late emerging low priority conjunctive representation.

In summary, we do not have statistical evidence of a time by effect interaction that allows us to draw strong inferences about timing. Nonetheless, even the patterns we observe are inconsistent with a late emerging low priority conjunctive representation. And if anything, they support a late decline in the untested high priority conjunctive representation. This pattern of the result of the high priority conjunction being sustained until late, even when it is untested, is also notable in light of our observation that the strength of the high priority conjunctive representation interferes behavior when the low priority item is tested, but not vice versa. We now address this point about the timing directly in the results (pg. 15-16) and the discussion (pg. 21), and we include the response locked results in the main text along with the stimulus locked result including exploratory analyses reported here.

Reviewer #3 (Public Review):

This study aims to address the important question of whether working memory can hold multiple conjunctive task representations. The authors combined a retro-cue working memory paradigm with their previous task design that cleverly constructed multiple conjunctive tasks with the same set of stimuli, rules, and responses. They used advanced EEG analytical skills to provide the temporal dynamics of concurrent working memory representation of multiple task representations and task features (e.g., stimulus and responses) and how their representation strength changes as a function of priority and task relevance. The results generally support the authors' conclusion that multiple task representations can be simultaneously manipulated in working memory.

We appreciate these helpful comments, and were pleased that the reviewer shares our view that these results may be broadly impactful.

Author Response

Reviewer #2 (Public Review):

Reviewer #2 was critical of every aspect of our manuscript and we were disappointed that they failed to appreciate the significance of our findings. However, we have responded to each point as described below:

1) The experiment displayed in Figure 5 is deeply flawed for multiple reasons and should be removed from the manuscript entirely. A Michaelis-Menton plot compares the initial rate of a reaction versus substrate concentration. Instead, the authors plotted the fraction of SsrB that is phosphorylated after 10 minutes at various substrate concentrations. Such a plot must reach saturation because the enzyme is limiting, whereas it is not always possible to achieve saturation in a genuine Michaelis-Menton plot. Because no reaction rates were measured, it is not possible to derive kcat values from the data.

Mea culpa. We now plot our phosphorylation data and describe the mid-point as a k0.5 and have removed Fig. 1g. When we directly compare the H12 mutant to wt at neutral pH, its phosphorylation level is less compared to the wt (see new Fig. 4a). The wt phosphorylation is reduced at acid pH, (Fig 4b), but with His12Q, there was no difference in phosphorylation between neutral and acid pH (Fig 4c). It is important to include this data, because in RcsB, a close homolog of SsrB, an H12A mutant was not phosphorylated by acetyl phosphate and it was incapable of binding to DNA, unlike what we show here with SsrB.

(i) Increasing the concentration of the phosphoramidite substrate increased ionic strength. Response regulator active sites contain many charged moieties and autophosphorylation of at least one response regulator (CheY) is inhibited by increasing ionic strength (PMID 10471801).

The reviewer raises some interesting points and they are based on CheY phosphorylation by small molecules. We have a long history of studying OmpR and SsrB as well as other RRs and we know that they can all behave very differently from “canonical signaling”. We examined the effect of ionic strength on SsrB phosphorylation and it was relatively insensitive to changes in ionic strength (our original buffer was 267-430 mOsm and in each case, we have 90% phosphorylation). However, we repeated all of the phosphorylation experiments and kept ionic strength constant. These data are now presented in the revised manuscript.

(ii) Autophosphorylation with phosphoramidite is pH dependent because the nitrogen on the donor must be protonated to form a good leaving group (PMID 9398221). The pKa of phosphoramidite is ~8. Therefore, the fraction of phosphoramidite that is reactive (i.e., protonated) will be very different at pH 6.1 and 7.4.

We are aware of those findings, but we are comparing the H12 mutant with the wt protein in each case. There is no reason to believe that the presence of the mutant should alter the phosphoramidate substrate, so we are comparing how the wt phosphorylation compares with the mutant (Fig 4b, c).

(iii) Response regulator autophosphorylation absolutely depends on the presence of a divalent metal ion (usually Mg2+) in the active site (PMID 2201404). There is no guarantee that the 20 mM Mg2+ included in the reaction is sufficient to saturate SsrB. Furthermore, as the authors themselves note, the amino acid at SsrB position 12 is likely to affect the affinity of Mg2+ binding. Therefore, the fraction of SsrB that is reactive (i.e. has Mg2+ bound) may differ between wildtype and the H12Q mutant, and/or between wildtype at different pHs (because the protonation state of His12 changes).

This is exactly the point that we are making. And why we varied the magnesium concentration (increasing to 50-100 mM). There was a slight increase in phosphorylation at 50 mM MgCl2 compared to 20 mM, and only a slight increase between 50 and 100 mM at pH 6.1. The revised phosphorylation experiments all contain 100 mM MgCl2.

2) The data in Figures 1abcd and 3de are clearly sigmoidal rather than hyperbolic, indicating cooperativity. However, there are insufficient data points between the upper and lower bounds to accurately calculate the Hill coefficient or KD values. This limitation of the data means that comparisons of apparent Hill coefficient or KD values under different conditions cannot be the basis of credible conclusions.

We respectfully disagree. In every curve that we provide, there is at least one data point in the transition between low and high binding. With the mutant H12Q, we did manage to get two data points in the transition and the KD was the same as the wildtype (Fig. 2). We provide an analysis of the binding curve which nicely demonstrates the range of KD values based on the lowest and highest error in the point (132-168 nM) and it doesn’t significantly change the value (this is now shown in Fig.1– figure supplement 1). The very high affinity we observed at pH 6.1 (KD ~5 nM) makes the range of possibilities between 4-8 nM (i.e. still VERY high affinity). These range in affinities at neutral and acid pH are very reminiscent of affinities we measured for OmpR and OmpR~P at the porin promoters, suggesting that acid pH puts SsrB in an activated state even in the absence of phosphorylation. A similar argument holds for the Hill coefficient (see Figure).

3) There are hundreds of receiver domain structures in PDB. There is some variation, but to a first approximation receiver domain structures, all exhibit an (alpha/beta)5 fold. The structure of SsrB predicted by i-TASSER breaks the standard beta-2 strand into two parts, which throws off the numbering for subsequent beta strands. Given the highly conserved receiver domain fold, I am skeptical that the predicted i-TASSER structure is correct or adds any value to the manuscript. If the authors wish to retain the structure of the manuscript, then they should point out the unusual feature and the consequence of strand numbering.

We now include a new model based on the RcsB/DNA crystal structure that eliminates this problem (see new Fig.2– figure supplement 2). We have replaced this model with an Alphafold prediction that was energy minimized to align with the RcsB dimer crystal structure (Fig.5– figure supplement 2). This model retains the original (beta/alpha)5 fold, so the classical numbering is retained.

4) The detailed predictions of active site structure in Supplementary Figure 5 are not physiologically relevant because Mg2+ was not included in the simulation. The presence of a divalent cation binding to Asp10 and Asp11 is likely to substantially alter interactions between Asp 10, Asp11, His12, and Lys109.

See response to 1iii, above and new Fig.5– figure supplement 2. Author response image 1 is a zoomed-in snapshot of supplementary Figure 8c that has been modelled using the RcsB dimer bound to BeF3 and Mg2+(6ZIX). Both the i-TASSER and Alphafold model receiver domains align well with this structure, and the polar contacts and pi-cation interactions made by His12 are maintained.

Author response image 1.

5) The authors present an AlphaFold model of an SsrB dimer, and note that His12 is at the dimer interface. However, the authors also believe that a higher-order oligomer of SsrB binds to DNA in a pH-dependent manner. Do the authors have any suggestions or informed speculation about how His12 might affect higher-order oligomerization than dimerization?

As mentioned to point 3, above, we now include a new model of an SsrB dimer bound to DNA based on our NMR structure of the CTD and the RcsB/DNA structure. In the RcsB paper, they also have evidence for a higher-order oligomer in the crystal structure of unphosphorylated (and BeF3-) RcsB, which showed an asymmetric unit containing 6 molecules of RcsB, which form 3 dimers arranged in a hexameric structure that resembles a cylinder. This configuration involves a crossed conformation with the REC of one molecule interacting with the DBD of another and interestingly, His12 is interacting with the DBD of another molecule. We modelled an SsrB oligomer structure using the RcsB hexamer as a template and have included it as a new figure (see Fig.5– figure supplement 3) and in the revised discussion (lines 432-448).

Author Response

Reviewer #1 (Public Review):

1) One nagging concern is that the category structure in the CNN reflects the category structure baked into color space. Several groups (e.g. Regier, Zaslavsky, et al) have argued that color category structure emerges and evolves from the structure of the color space itself. Other groups have argued that the color category structure recovered with, say, the Munsell space may partially be attributed to variation in saturation across the space (Witzel). How can one show that these properties of the space are not the root cause of the structure recovered by the CNN, independent of the role of the CNN in object recognition?

We agree that there is overlap with the previous studies on color structure. In our revision, we show that color categories are directly linked to the CNN being trained on the objectrecognition task and not the CNN per se. We repeated our analysis on a scene-trained network (using the same input set) and find that here the color representation in the final layer deviates considerably from the one created for object classification. Given the input set is the same, it strongly suggests that any reflection of the structure of the input space is to the benefit of recognizing objects (see the bottom of “Border Invariance” section; Page 7). Furthermore, the new experiments with random hue shifts to the input images show that in this case stable borders do not arise, as might be expected if the border invariance was a consequence of the chosen color space only.

A crucial distinction to previous results is also, is that in our analysis, by replacing the final layer, specifically, we look at the representation that the network has built to perform the object classification task on. As such the current finding goes beyond the notion that the color category structure is already reflected in the color space.

2) In Figure 1, it could be useful to illustrate the central observation by showing a single example, as in Figure 1 B, C, where the trained color is not in the center of the color category. In other words, if the category structure is immune to the training set, then it should be possible to set up a very unlikely set of training stimuli (ones that are as far away from the center of the color category while still being categorized most of the time as the color category). This is related to what is in E, but is distinctive for two reasons: first, it is a post hoc test of the hypothesis recovered in the data-driven way by E; and second, it would provide an illustration of the key observation, that the category boundaries do not correspond to the median distance between training colors. Figure 5 begins to show something of this sort of a test, but it is bound up with the other control related to shape.

We have now added a post-hoc test where we shift the training bands from likely to unlikely positions using the original paradigm: Retraining output layers whilst shifting training bands from the left to the right category-edge (in 9 steps) we can see the invariance to the category bounds specifically (see Supp. Inf.: Figure S11). The most extreme cases (top and bottom row) have the training bands right at the edge of the border, which are the interesting cases the reviewer refers to. We also added 7 steps in between to show how the borders shift with the bands.

Similarly, if the claim is that there are six (or seven?) color categories, regardless of the number of colors used to train the data, it would be helpful to show the result of one iteration of the training that uses say 4 colors for training and another iteration of the training that uses say 9 colors for training.

We have now included the figure presented in 1E, but for all the color iterations used (see SI: Figure S10. We are also happy to include a single iteration, but believe this gives the most complete view for what the reviewer is asking.

The text asserts that Figure 2 reflects training on a range of color categories (from 4 to 9) but doesn’t break them out. This is an issue because the average across these iterations could simply be heavily biased by training on one specific number of categories (e.g. the number used in Figure 1). These considerations also prompt the query: how did you pick 4 and 9 as the limits for the tests? Why not 2 and 20? (the largest range of basic color categories that could plausibly be recovered in the set of all languages)?

The number of output nodes was inspired by the number of basic color categories that English speakers observe in the hue spectrum (in which a number of the basic categories are not represented). We understand that this is not a strong reason, however, unfortunately the lack of studies on color categories in CNNs forced us to approach this in an explorative manner. We have adapted the text to better reflect this shortcoming (Bottom page 4). Naturally if the data would have indicated that these numbers weren’t a good fit, we would have adapted the range. (if there were more categories, we would have expected more noise and we would have increased the number of training bands to test this). As indicated above, we have now also included the classification plots for all the different counts, so the reader can review this as well (SI: Section 9).

3) Regarding the transition points in Figure 2A, indicated by red dots: how strong (transition count) and reliable (consistent across iterations) are these points? The one between red and orange seems especially willfully placed.

To answer the question on the consistency we have now included a repetition of the ResNet18, with the ResNet34, ResNet50 and ResNet101 in the SI (section 1). We have also introduced a novel section presenting the result of alternate CNNs to the SI (section S8). Despite small idiosyncrasies the general pattern of results recurs.

Concerning the red-orange border, it was not willfully placed, but we very much understand that in isolation it looks like it could simply be the result of noise. Nevertheless, the recurrence of this border in several analyses made us confident that it does reflect a meaningful invariance. Notably:

• We find a more robust peak between red and orange in the luminance control (SI section 3).

• The evolutionary algorithm with 7 borders also places a border in this position.

• We find the peak recurs in the Resnet-18 replication as well as several of the deeper ResNets and several of the other CNNs (SI section 1)

• We also find that the peak is present throughout the different layers of the ResNet-18.

4) Figure 2E and Figure 5B are useful tests of the extent to which the categorical structure recovered by the CNNs shifts with the colors used to train the classifier, and it certainly looks like there is some invariance in category boundaries with respect to the specific colors uses to train the classifier, an important and interesting result. But these analyses do not actually address the claim implied by the analyses: that the performance of the CNN matches human performance. The color categories recovered with the CNN are not perfectly invariant, as the authors point out. The analyses presented in the paper (e.g. Figure 2E) tests whether there is as much shift in the boundaries as there is stasis, but that’s not quite the test if the goal is to link the categorical behavior of the CNN with human behavior. To evaluate the results, it would be helpful to know what would be expected based on human performance.

We understand the lack of human data was a considerable shortcoming of the previous version of the manuscript. We have now collected human data in a match-to-sample task modeled on our CNN experiment. As with the CNN we find that the degree of border invariance does fluctuate considerably. While categorical borders are not exact matches, we do broadly find the same category prototypes and also see that categories in the red-to-yellow range are quite narrow in both humans and CNNs. Please, see the new “Human Psychophysics” (page 8) addition in the manuscript for more details.

5) The paper takes up a test of color categorization invariant to luminance. There are arguments in the literature that hue and luminance cannot be decoupled-that luminance is essential to how color is encoded and to color categorization. Some discussion of this might help the reader who has followed this literature.

We have added some discussion of the interaction between luminance and color categories (e.g., Lindsay & Brown, 2009) at the bottom of page 6/ top of page 7. The current analysis mainly aimed at excluding that the borders are solely based on luminance.

Related, the argument that “neighboring colors in HSV will be neighboring colors in the RGB space” is not persuasive. Surely this is true of any color space?

We removed the argument about “neighboring colors”. Our procedure requires the use of a hue spectrum that wraps around the color space while including many of the highly saturated colors that are typical prototypes for human color categories. We have elected to use the hue spectrum from the HSV color space at full saturation and brightness, which is represented by the edges of the RGB color cube. As this is the space in which our network was trained, it does not introduce any deformations into the color space. Other potential choices of color space either include strong non-linear transformations that stretch and compress certain parts of the RGB cube, or exclude a large portion of the RGB gamut (yellow in particular).

We have adapted the text to better reflect our reasoning (page 6, top of paragraph 2).

6) The paper would benefit from an analysis and discussion of the images used to originally train the CNN. Presumably, there are a large number of images that depict manmade artificially coloured objects. To what extent do the present results reflect statistical patterns in the way the images were created, and/or the colors of the things depicted? How do results on color categorization that derive from images (e.g. trained with neural networks, as in Rosenthal et al and presently) differ (or not) from results that derive from natural scenes (as in Yendrikhovskij?).

We initially hoped we could perhaps analyze differences between colors in objects and background like in Rosenthal, unfortunately in ImageNet we did not find clear differences between pixels in the bounding boxes of objects provided with ImageNet and pixels outside these boxes (most likely because the rectangular bounding boxes still contain many background pixels). However, if we look at the results from the K-means analysis presented in Figure S6 (Suppl. Inf.) of the supplemental materials and the color categorization throughout the layers in the objecttrained network (end of the first experiment on page 7) as well as the color categorization in humans (Human Psychophysics starting on page 8), we see very similar border positions arise.

7) It could be quite instructive to analyze what's going on in the errors in the output of the classifiers, as e.g. in Figure 1E. There are some interesting effects at the crossover points, where the two green categories seem to split and swap, the cyan band (hue % 20) emerges between orange and green, and the pink/purple boundary seems to have a large number of green/blue results. What is happening here?

One issue with training the network on the color task, is that we can never fully guarantee that the network is using color to resolve the task and we suspected that in some cases the network may rely on other factors as well, such as luminance. When we look at the same type of plots for the luminance-controlled task (see below left) presented in the supplemental materials we do not see these transgressions. Also, when we look at versions of the original training, but using more bands, luminance will be less reliable and we also don’t see these transgressions (see right plot below).

8) The second experiment using an evolutionary algorithm to test the location of the color boundaries is potentially valuable, but it is weakened because it pre-determines the number of categories. It would be more powerful if the experiment could recover both the number and location of the categories based on the "categorization principle" (colors within a category are harder to tell apart than colors across a color category boundary). This should be possible by a sensible sampling of the parameter space, even in a very large parameter space.

The main point of the genetic algorithm was to see whether the border locations would be corroborated by an algorithm using the principle of categorical perception. Unfortunately, an exact approach to determining the number of borders is difficult, because some border invariances are clearly stronger than others. Running the algorithm with the number of borders as a free parameter just leads to a minimal number of borders, as 100% correct is always obtained when there is only one category left. In general, as the network can simply combine categories into a class at no cost (actually, having less borders will reduce noise) it is to be expected that less classes will lead to better performance. As such, in estimating what the optimal category count would be, we would need to introduce some subjective trade-off between accuracy and class count.

9) Finally, the paper sets itself up as taking "a different approach by evaluating whether color categorization could be a side effect of learning object recognition", as distinct from the approach of studying "communicative concepts". But these approaches are intimately related. The central observation in Gibson et al. is not the discovery of warm-vscool categories (these as the most basic color categories have been known for centuries), but rather the relationship of these categories to the color statistics of objects-those parts of the scene that we care about enough to label. This idea, that color categories reflect the uses to which we put our color-vision system, is extended in Rosenthal et al., where the structure of color space itself is understood in terms of categorizing objects versus backgrounds (u') and the most basic object categorization distinction, animate versus inanimate (v'). The introduction argues, rightly in our view, that "A link between color categories and objects would be able to bridge the discrepancy between models that rely on communicative concepts to incorporate the varying usefulness of color, on the one hand, and the experimental findings laid out in this paragraph on the other". This is precisely the link forged by the observation that the warmcool category distinction in color naming correlates with object-color statistics (Gibson, 2017; see also Rosenthal et al., 2018). The argument in Gibson and Rosenthal is that color categorization structure emerges because of the color statistics of the world, specifically the color statistics of the parts of the world that we label as objects, which is the same approach adopted by the present work. The use of CNNs is a clever and powerful test of the success of this approach.

We are sorry we did not properly highlight the enormous importance of these two earlier papers in our previous version of the manuscript. We have now elaborated our description of Gibson’s work to better reflect the important relation between the usefulness of colors and color categories (Page 2, middle and Page 19 par. above methods). We think our work nicely extends the earlier work by showing that their approach works even at a more general level with more color categories,

Author Response

Reviewer #1 (Public Review):

Using health insurance claims data (from 8M subjects), a retrospective propensity score matched cohort study was performed (450K in both groups) to quantify associations between bisphosphonate (BP) use and COVID- 19 related outcomes (COVID-19 diagnosis, testing and COVID-19 hospitalization. The observation periods were 1-1-2019 till 2-29-2020 for BP use and from 3-1-2020 and 6-30-2020 for the COVID endpoints. In primary and sensitivity analyses BP use was consistently associated with lower odds for COVID-19, testing and COVID-19 hospitalization.

The major strength of this study is the size of the study population, allowing a propensity-based matched- cohort study with 450K in both groups, with a sizeable number of COVID-19 related endpoints. Health insurance claims data were used with the intrinsic risk of some misclassification for exposure. In addition there probably is misclassification of endpoints as testing for COVID-19 was limited during the study period. Furthermore, the retrospective nature of the study includes the risk of residual confounding, which has been addressed - to some extent - by sensitivity analyses.

In all analyses there is a consistent finding that BP exposure is associated with reduced odds for COVID-19 related outcomes. The effect size is large, with high precision.

The authors extensively discuss the (many) potential limitations inherent to the study design and conclude that these findings warrant confirmation, preferably in intervention studies. If confirmed BP use could be a powerful adjunct in the prevention of infection and hospitalization due to COVID-19.

We thank the reviewer for this overall very positive feedback. We appreciate the reviewer's comments regarding the potential risks associated with misclassification of exposure and other potential limitations, which we have sought to address in a number of sensitivity analyses and are also addressing in the discussion of our paper. In addition, as noted by the reviewer, the observed effect size of BP use on COVID-19 related outcomes is large, with high precision, which we feel is a strong argument to explore this class of drugs in further prospective studies.

Reviewer #2 (Public Review):

The authors performed a retrospective cohort study using claims data to assess the causal relationship between bisphosphonate (BP) use and COVID-19 outcomes. They used propensity score matching to adjust for measured confounders. This is an interesting study and the authors performed several sensitivity analyses to assess the robustness of their findings. The authors are properly cautious in the interpretation of their results and justly call for randomized controlled trials to confirm a causal relationship. However, there are some methodological limitations that are not properly addressed yet.

Strengths of the paper include:

(A) Availability of a large dataset.

(B) Using propensity score matching to adjust for confounding.

(C) Sensitivity analyses to challenge key assumptions (although not all of them add value in my opinion, see specific comments)

(D) Cautious interpretation of results, the authors are aware of the limitations of the study design.

Limitation of the paper are:

(A) This is an observational study using register data. Therefore, the study is prone to residual confounding and information bias. The authors are well aware of that.

(B) The authors adjusted for Carlson comorbidity index whereas they had individual comorbidity data available and a dataset large enough to adjust for each comorbidity separately.

(C) The primary analysis violates the positivity assumption (a substantial part of the population had no indication for bisphosphonates; see specific comments). I feel that one of the sensitivity analyses 1 or 2 would be more suited for a primary analysis.

(D) Some of the other sensitivity analyses have underlying assumptions that are not discussed and do not necessarily hold (see specific comments).

In its current form the limitations hinder a good interpretation of the results and, therefore, in my opinion do not support the conclusion of the paper.

The finding of a substantial risk reduction of (severe) COVID-19 in bisphosphonate users compared to non- users in this observational study may be of interest to other researchers considering to set up randomized controlled trials for evaluation of repurpose drugs for prevention of (severe) COVID-19.

We thank the reviewer for the insightful comments and questions related to our manuscript. Our response to the concerns regarding limitations of our study is as follows:

(A) We agree that there is likely residual confounding and information bias due to use of US health insurance claims datasets which do not include information on certain potentially relevant variables. Nonetheless, given the large effect size and precision of our analysis, we feel that our findings support our main conclusion that additional prospective trials appear warranted to further explore whether BPs might confer a meaure of protection against severe respiratory infections, including COVID-19. We have added a sentence on the second page of our Discussion (line 859-860) to emphasize this point: "Specifically, there is the potential that key patient characteristics impacting outcomes could not be derived from claims data."

(B) The progression of this study mirrors the real-world performance of the analysis where we initially used the CCI in matching to control for comorbidity burden on a broader scale. This was our a priori approach. After observing large effect sizes, we performed more stringent matching for sensitivity analyses 1 and 2. Irrespective of the matching strategy chosen, effect sizes remained similar for all outcome parameters. Therefore, we elected to include both the primary analysis and the sensitivity analyses with more stringent matching in order to more transparently show what was done in entirety during our analyses, as we feel it displays all of the efforts taken to identify sources of unmeasured confounding which could have impacted our results.

(C) We agree that the positivity assumption is a key factor to consider when building comparable treatment cohorts. We also agree that it is the important to separately perform the analysis for either all patients with an indication for use of BPs and for other anti-osteoporosis medications, as we have done in our analysis of the Osteo-Dx-Rx cohort and Bone-Rx cohort, respectively. However, we did not have sufficient data, a priori, to determine whether BP users would be more similar in their risk of COVID-19 outcomes to non- users or to other users of anti-resorptive medications. In addition, we believe that this specific limitation does not negate our findings in the primary analysis for the following reasons: (1) ‘Type of Outcome’: the outcomes in this study are related to infectious disease and are not direct clinical outcomes of any known treatment benefits of BPs. The clinical benefits being assessed - impact of BP use on COVID-19-related outcomes - were essentially unknown at the time of the study data; this fact mitigates the impact of any violation of the positivity assumption; and (2) ‘Clinical Population’: after propensity score matching, both the BP user and the BP non-user group in the primary analysis mainly consisted of older females (90.1% female, 97.2% age>50), which is the main population with clinical indications for BP use. According to NCHS Data Brief No. 93 (April 2012) released by the CDC, ~75% and 95% of US women between 60-69 and 70-79 suffer from either low bone mass or osteoporosis, respectively, and essentially all women (and 70% of men) above age 80 suffer from these conditions, which often go undiagnosed (https://www.cdc.gov/nchs/data/databriefs/db93.pdf). Women aged 60 and older make up ~75% of our study population (Table 1). Although bone density measurements are not available for non- BP users in the matched primary cohort, there is a high probability that the incidence of osteoporosis and/or low bone mass in these patients was similar to the national average. This justifies the assumption that BP therapy was indicated for most non-BP users in the matched primary cohort. Arguably, for these patients the positivity assumption was not violated.

(D) We will discuss in detail below the specific issues raised by the reviewer regarding our sensitivity analyses. In general we acknowledge that individual analytical and/or matching approaches may each have their own limitations, but the analyses performed herein were done to test in a systematic fashion the different critical threats to the validity of our initial results in the primary cohort analysis, which were based on a priori-defined methods and yielded a large and robust effect size. Thus, the individual sensitivity analyses should be considered in the greater context of the entire project.

Specific comments (in order of manuscript):

Methods:

Line 158: it is unclear how the authors dealt with patients who died during the follow-up period. The wording suggests they were excluded which would be inappropriate.

When this study was executed, we were unable to link the patient-level US insurance claims data with patient-level mortality data due to HIPAA concerns. Therefore, line 158 (now 177) defines continuous insurance coverage during the observation period as a verifiable eligibility criterion we used for patient inclusion. It was necessary to disqualify individuals who discontinued insurance coverage for a variety of reasons, e.g. due to loss or change of coverage, relocation etc., but our approach also eliminated patients who died. Appendix 3 (line 2449ff) describes methods we employed post hoc to assess how censoring due to death could have impacted our analyses. We discuss our conclusions from this post hoc analysis in the main text (lines 1053-1058) as follows: "An additional limitation is potential censoring of patients who died during the observation period, resulting in truncated insurance eligibility and exclusion based on the continuous insurance eligibility requirement. However, modelling the impact of censoring by using death rates observed in BP users and non-users in the first six months of 2020 and attributing all deaths as COVID-19-related did not significantly alter the decreased odds of COVID-19 diagnosis in BP users (see Appendix 3)."

Why did the authors use CCI for propensity matching rather than the individual comorbid conditions? I presume using separate variables will improve the comparability of the cohorts. The authors discuss imbalances in comorbidities as a limitation but should rather have avoided this.

CCI was the a priori approach defined at the study outset and was chosen due to the widespread use and understanding of this score. The general CCI score was originally planned for matching in order to have the largest possible study population since we did not know how many patients would meet all criteria as well as have an event of interest. After realizing we had adequate sample size to power matching using stricter criteria, we proceeded to perform subsequent sensitivity analyses on more stringently matched cohorts (sensitivity analysis 2).

Line 301-10: it seems unnecesary to me to adjust for the given covariates while these were already used for propensity score matching (except comorbidities, but see previous comment). The manuscript doesn't give a rationale why did the authors choose for this 'double correction'.

The following language was added to the methods section (lines 325-327): “Demographic characteristics used in the matching procedure were also included in the final outcome regressions to control for the impact of those characteristics on outcomes modelled.”

The following language was added to the Discussion section regarding the potential limitations of our srudy (lines 1078-1085): “Another limitation in the current study is related to a potential ‘double correction’ of patient characteristics that were included in both the propensity score matching procedure as well as the outcome regression modelling, which could lead to overfitting of the regression models and an overestimation of the measured treatment effect. Covariates were included in the regression models since these characteristics could have differential impacts on the outcomes themselves, and our results show that the adjusted ORs were in fact larger (showing a decreased effect size) when compared to the unadjusted ORs, which show the difference in effect sizes of the matched populations alone.”

In causal research a very important assumption is the 'positivity assumption', which means that none of the individuals has a probability of zero or one to be exposed. Including everyone would therefore not be appropriate. My suggestion is to include either all patients with an indication (based on diagnosis) or all that use an anti-osteoporosis (AOP) drug (or one as the primary and the other as the sensitivity analysis) instead of using these cohorts as sensitivity analyses. The choice should in my opinion be based on two aspects: whether it is likely that other AOP drugs have an effect on the COVID-19 outcomes and whether BP users are deemed to be more similar (in their risk of COVID-19 outcomes) to non-users or to other AOP drug users. Or alternatively, the authors might have discussed the positivity assumption and argue why this is not applicable to their primary analysis.

The following text has been added to the Discussion section addressing potential limitations of our study (lines 987-1009): " Another potential limitation of this study relates to the positivity assumption, which when building comparable treatment cohorts is violated when the comparator population does not have an indication for the exposure being modelled 56. This limitation is present in the primary cohort comparisons between BP users and BP non-users, as well as in the sensitivity analyses involving other preventive medications. This limitation, however, is mitigated by the fact that the outcomes in this study are related to infectious disease and are not direct clinical outcomes of known treatment benefits of BPs. The fact that the clinical benefits being assessed – the impact of BPs on COVID-related outcomes – was essentially unknown clinically at the time of the study data minimizes the impact of violation of the positivity assumption. Furthermore, our sensitivity analyses involving the “Bone-Rx” and “Osteo-Dx- Rx” cohorts did not suffer this potential violation, and the results from those analyses support those from the primary analysis cohort comparisons. Moreover, we note that the propensity score matched BP users and BP non-users in the primary analysis cohort mainly consisted of older females. According to the CDC, ~75% and 95% of US women between 60-69 and 70-79 suffer from either low bone mass or osteoporosis, respectively (https://www.cdc.gov/nchs/data/databriefs/db93.pdf). Essentially all women (and 70% of men) above age 80 suffer from these conditions, which often go undiagnosed. Women aged 60 and older represent ~75% of our study population (Table 1). Although bone density measurements are not available for non-BP users in the matched primary cohort, there is a high probability that the incidence of osteoporosis and/or low bone mass in these patients was similar to the national average.Thus, BP therapy would have been indicated for most non-BP users in the matched primary cohort, and arguably, for these patients the positivity assumption was not violated."

Sensitivity Analysis 3: Association of BP-use with Exploratory Negative Control Outcomes: what is the implicit assumption in this analysis? I think the assumption here is that any residual confounding would be of the same magnitude for these outcomes. But that depends on the strength of the association between the confounder and the outcome which needs not be the same. Here, risk avoiding behavior (social distancing) is the most obvious unmeasured confounder, which may not have a strong effect on other health outcomes. Also it is unclear to me why acute cholecystitis and acute pancreatitis-related inpatient/emergency-room were selected as negative controls. Do the authors have convincing evidence that BPs have no effect on these outcomes? Yet, if the authors believe that this is indeed a valid approach to measure residual confounding, I think the authors might have taken a step further and present ORs for BP → COVID-19 outcomes that are corrected for the unmeasured confounding. (e.g. if OR BP → COVID-19 is ~ 0.2 and OR BP → acute cholecystitis is ~ 0.5, then 'corrected' OR of BP → COVID-19 would be ~ 0.4.

We appreciate the reviewer’s thoughtful comments regarding the differential strength of the association between unmeasured confounders and outcome. We had initially selected acute cholecystitis and pancreatitis-related inpatient and emergency room visits as negative controls because we deemed them to be emergent clinical scenarios that should not be impacted by risk avoiding behavior. However, upon further search, we identified several publications that suggest a potential impact of osteoporosis and/or BPs on gallbladder diseases (DOIhttps://doi.org/10.1186/s12876-014-0192-z; http://dx.doi.org/10.1136/annrheumdis-2017-eular.3900), thus calling the validity our strategy into question. We therefore agree that the designation of negative control outcomes is problematic and adds relatively little to the overall story. Therefore, we have removed these analyses from the revised manuscript.

Sensitivity Analysis 4: Association of BP-use with Exploratory Positive Control Outcomes: this doesn't help me be convinced of the lack of bias. If previous researchers suffered from residual confounding, the same type of mechanisms apply here. (It might still be valuable to replicate the previous findings, but not as a sensitivity analysis of the current study).

We agree that the same residual confounding in previous research papers could be present in our study. Nonetheless, it was important to assess whether our analysis would be potentially subject to additional (or different) confounding due to the nature of insurance claims data as compared to the previous electronic record-based studies. Therefore, it was relevant to see if previous findings of an association between BP use and upper respiratory infections are observable in our cohort.

The second goal of sensitivity analysis #4 (now #3) was to see whether associations could be found on different sets of respiratory infection-based conditions, both during the time of the pandemic/study period as well as during the pre-pandemic time, i.e. before medical care in the US was significantly impacted by the pandemic. In light of these considerations, we feel that sensitivity analysis 4 adds value by showing consistency in our core findings.

Sensitivity Analysis 5: Association of Other Preventive Drugs with COVID-19-Related Outcomes: Same here as for sensitivity analysis 3: the assumption that the association of unmeasured confounders with other drugs is equally strong as for BPs. Authors should explicitly state the assumptions of the sensitivity analyses and argue why they are reasonable.

The following sentence was added to the Discussion section (lines 1019-1020): “ "These analyses were based on the assumption that the association of unmeasured confounders with other drugs is comparable in magnitude and quality as for BPs."

Results: The data are clearly presented. The C-statistic / ROC-AUC of the propensity model is missing.

Unfortunately, a significant amount of time has passed since execution of our original analysis of the Komodo dataset by our co-authors at Cerner Enviza. To date, our ability to perform follow-up studies with the Komodo dataset (which is exclusively housed on Komodo's secure servers) has become limited because business arrangements between these companies have been terminated, and the pertinent statistical software is no longer active. This issue prevents us from attaining the original C-statistic and ROC-AUC information, however, we were able to extract the actual; propensity scores themselves for the base cohort matching (BP-users versus non-users). The table below illustrates that the distribution of propensity scores for the base cohort match ranged from <0.01 to a max of 0.49, with 81.4% of patients having a propensity score of 10-49%, and 52.9% of patients having a propensity score of 20-49%. This distribution is unlikely to reflect patients who had a propensity score of either all 0 or all 1.

Discussion:

When discussing other studies the authors reduce these results to 'did' or 'did not find an association'. Although commonly practiced, it doesn't justify the statistical uncertainty of both positive and negative findings. Instead I encourage the authors to include effect estimates and confidence intervals. This is particularly relevant for studies that are inconclusive (i.e. lower bound of confidence interval not excluding a clinically relevant reduction while upper bound not excluding a NULL-effect).

We appreciate the reviewer’s suggestion and have added this information on p.21/22 in the Discussion.

Line 1145 "These retrospective findings strongly suggest that BPs should be considered for prophylactic and/or therapeutic use in individuals at risk of SARS-CoV-2 infection." I agree for prophylactic use but do not see how the study results suggest anything for therapeutic use.

We have removed “and/or therapeutic use” from this sentence (line 1088-1090).

The authors should discuss the acceptability of using BPs as preventive treatment (long-term use in persons without osteoporosis or other indication for BPs). This is not my expertise but I reckon there will be little experience with long-term inhibiting osteoblasts in people with healthy bones. The authors should also discuss what prospective study design would be suitable and what sample size would be needed to demonstrate a reasonable reduction. (Say 50% accounting for some residual confounding being present in the current study.)

Although BPs are also used in pediatric populations and in patients without osteoporosis (for example, patients with malignancy), we do recognize the lack of long-term safety data in use of BPs as preventative treatments. We tried to partially address this concern in our sub-stratified analysis of COVID-19 related outcomes and time of exposure to BP. Reassuringly, we observed that patients newly prescribed alendronic acid in February 2020 also had decreased odds of COVID-19 related outcomes (Figure 3B), suggesting that the duration of BP treatment may not need to be long-term. This was further discussed in the last paragraph of our Discussion where we state that " BP use at the time of infection may not be necessary for protection against COVID-19. Rather, our results suggest that prophylactic BP therapy may be sufficient to achieve a potentially rapid and sustained immune modulation resulting in profound mitigation of the incidence and/or severity of infections by SARS- CoV-2."

We agree that a future prospective study on the effect of BPs on COVID-19 related outcomes will require careful consideration of the study design, sample size, statistical power etc. However, we feel that a detailed discussion of these considerations is beyond the scope of the present study.

The authors should discuss the fact that confounders were based on registry data which is prone to misclassification. This can result in residual confounding.

Some potential sources of misclassification have been discussed on line 932-948. In addition, the following language was added (line 970-985): "Additionally, limitations may be present due to misclassification bias of study outcomes due to the specific procedure/diagnostic codes used as well as the potential for residual confounding occurring for patient characteristics related to study outcomes that are unable to be operationalized in claims data, which would impact all cohort comparisons. For SARS- CoV-2 testing, procedure codes were limited to those testing for active infection, and therefore observations could be missed if they were captured via antibody testing (CPT 86318, 86328). These codes were excluded a priori due to the focus on the symptomatic COVID-19 population. Furthermore, for the COVID-19 diagnosis and hospitalization outcomes, all events were identified using the ICD-10 code for lab-confirmed COVID-19 (U07.1), and therefore events with an associated diagnosis code for suspected COVID-19 (U07.2) were not included. This was done to have a more stringent algorithm when identifying COVID-19-related events, and any impact of events identified using U07.2 is considered minimal, as previous studies of the early COVID-19 outbreak have found that U07.1 alone has a positive predictive value of 94%55, and for this study U07.1 captured 99.2%, 99.0%, and 97.5% of all COVID-19 patient-diagnoses for the primary, “Bone-Rx”, and “Osteo-Dx-Rx” cohorts, respectively."

Author Response:

Evaluation Summary:

The study provides evidence that specific transcriptional responses may underpin the observation that metabolic rates often scale inversely with body mass. The conclusions are supported by direct measurement of metabolic fluxes in mouse and rat livers, although generalizations to other settings remain to be rigorously tested. The study has broad implications for researching and studying animal metabolism and physiology.

We thank the reviewers and editors for this summary. We are pleased that they agree that the conclusions “are supported by direct measurements of metabolic fluxes in mouse and rat livers,” and that “the study has broad implications for researching and studying animal metabolism and physiology. While we fully agree that “generalizations to other settings remain to be rigorously tested,” we have now added a comment comparing our measured liver fluxes in rodents to those recently measured in people:

“While we did not have the capacity to measure liver fluxes in larger mammals in the current study, endogenous glucose production, VPC, and VCS previously measured using PINTA were 50-60% lower in overnight fasted humans than in rats (Petersen et al., 2019), assuming a liver size of 1,500 g in humans.”

Reviewer #1 (Public Review):

It is well established that the energy expenditure and metabolic rate of metazoan organisms scale inversely to body mass, based on the measurement of oxygen consumption and caloric intake. However, the underlying regulatory mechanisms for this observation are poorly defined. To investigate whether metabolic scaling is associated with reduced levels of transcription of metabolic genes in larger animals, the authors reviewed existing transcriptional datasets from liver tissues of five animals (mice, rats, monkeys, humans and cattle) with a 30,000-fold range in average adult body weights. They identified a number of metabolic genes in different pathways of central carbon metabolism whose expression inversely scaled with body size, a majority of which required oxygen, NAD/H or ATP/ADP. Metabolic flux studies on intact liver sections, as well as in live animals also revealed decreased liver metabolic fluxes in rats compared to mice. Interestingly, these differences were not observed in primary hepatocyte cultures, indicating that metabolic scaling is primarily regulated by cell-extrinsic factors and tissue context. These are interesting findings and highlight the importance of measuring metabolic processes in vivo. The measurement of cellular metabolic fluxes in different contexts (cultured, ex vivo tissue sections and live animals) is a major strength of this study. The lack of direct evidence that enzyme levels correlate with mRNA, and the absence of both transcriptional and enzyme activity measurements in cultured cells are potential weaknesses.

We are delighted, and thank Reviewer #1 for stating that “These are interesting findings and highlight the importance of measuring metabolic processes in vivo” and that “The measurement of cellular metabolic fluxes in different contexts (cultured, ex vivo tissue sections and live animals) is a major strength of this study.” In addition, we sincerely thank the reviewer for raising important weaknesses related to the importance of proteomics, transcriptional and enzyme activity measurements in cultured cells, and are pleased to have had the opportunity to add data to address each of these points.

Reviewer #2 (Public Review):

Akingbesote et al. aim to determine the molecular basis of metabolic scaling - the phenomenon that metabolic rates scale inversely with (0.75) body mass. More specifically, they test the hypothesis that expression of genes involved in the regulation of oxygen consumption and substrate metabolism as well as respective fluxes provide a molecular basis for metabolic scaling across five species: mice, rats, monkeys, humans, and cattle. To this end, Akingbesote et al. use publicly available transcriptomics data and identify genes that show decreasing (normalized) expression with increasing mass of organisms. This descriptive analysis is followed by discussing a few relevant examples and (KEGG) pathway enrichment analysis. The authors then used their published PINTA approach with data from their experiments with mice and rats to provide estimates of selected cytosolic and mitochondrial fluxes in vitro, ex vivo, and in vivo; these estimates are then employed in determining if metabolic fluxes scale. The conclusion drawn from these analyses is that estimates of selected fluxes do not differ in vitro between plated hepatocytes of mice and rats, but that differences can be detected using metabolic flux analysis in vivo. As a result, in vivo flux profiling is more relevant to assessing metabolic scaling.

The conclusions are only in part supported by the data and clarifications are needed both with respect to the analysis of transcriptomics data as well as flux estimates:

1. In looking for scaling in gene expression, the authors rely on the assumption that mRNA expression correlates well with protein abundance (citing Schwanhäusser et al., 2011); however, transcripts explain about 40% of variance in protein abundance (this observation holds across multiple species). Hence, the identified patterns based on the transcript data may have little implications for protein abundance or flux.

We agree that, despite the data in the cited publication, gene expression should not be assumed to directly correlate with protein expression, and the two certainly cannot be assumed – without data to equate to metabolic flux. We have removed the citation, and replaced it with proteomics data. Half of the genes available in the proteomics analysis which were found to correlate negatively with body size in our liver transcriptomics analysis also correlated negatively with body size at the level of liver protein expression:

Author Response Figure 1

Additionally, we analyzed available proteomics assessment of left ventricular expression of the three proteins observed to correlate negatively with body mass in the liver proteomics analysis. One of the three genes observed to correlate negatively with body mass in the proteomics analysis of liver, GLUL, was also shown to correlate negatively with body mass when its expression was assessed in the heart:

Author Response Figure 2

However, as discussed in our response to the editor’s point 1, we are limited by the available data, and fully acknowledge that without the capacity to statistically compare groups, we cannot make conclusive statements regarding the proteomics data.

Additionally, we have substantially softened the description of the implications of the transcriptomics data in the Abstract, Introduction, and Discussion, including: - Editing “Together, these data reveal that metabolic scaling extends beyond oxygen consumption to numerous other metabolic pathways, and is likely regulated at the level of gene and protein expression, enzyme activity, and substrate supply” to add the parameters in red. - Removing “Considering that mRNA expression correlates well with protein expression under basal conditions, especially for metabolic genes (Schwanhäusser et al., 2011), we used mRNA expression as a proxy for the relative abundance of metabolic enzymes.” - Added “Further analysis of liver proteomics revealed that approximately half of the genes in liver that scaled at the transcriptional level also scaled at the level of protein expression,” now linking gene expression to protein expression to metabolic flux. - Editing “Numerous metabolic genes…followed the pattern of metabolic scaling, and informed our isotope tracer based in vitro and in vivo metabolic flux studies” to “Numerous metabolic genes…followed the pattern of metabolic scaling. Further analysis of liver proteomics revealed that approximately half of the genes in liver that scaled at the transcriptional level also scaled at the level of protein expression. To determine if gene and protein expression would correlate with scaling at the level of metabolic flux, we performed a comprehensive assessment of liver metabolism in vivo and in vitro using modified Positional Isotopomer NMR Tracer Analysis (PINTA)…” - Edited “Taken together, this study demonstrates systems regulation of metabolic scaling: gene expression in livers showed that scaling occurs to regulate oxygen consumption and substrate supply, isotope-based tracer studies in mice and rats demonstrated the mechanistic function of these enzymes in vivo which was only apparent in the living organism rather than plated cells” to “Taken together, this study demonstrates systems regulation of the ordering of metabolic fluxes according to body size, and provides unique insight into the regulation of metabolic flux across species.” - Removed “Interestingly, the scaling of GPT and ADIPOR1 further suggest that there is dependence on extra-hepatic organs in the scaling of in vivo gluconeogenesis and fatty acid oxidation: that is, skeletal muscle supply of alanine for the liver mediated glucose-alanine cycle and adipose tissue-derived adiponectin signaling. These findings also suggests that the scaling of mitochondrial mass (Porter and Brand, 1995) or mitochondrial proton leak (Porter and Brand, 1993) cannot fully explain metabolic scaling.” - Added “However, it should be noted that metabolic scaling cannot fully be explained at the transcriptional level, because many rate-limiting enzymes in the metabolic processes measured in vivo did not scale at the transcriptional level, and only approximately half of genes that scaled at the level of mRNA scaled at the level of protein. Thus, it is likely that both transcriptional and other mechanisms – such as enzyme activity – are responsible for variations in metabolic flux per unit mass, inversely proportionally to body size. Additionally, the currently available data do not allow us to assess whether expression of certain isoforms of key metabolic enzymes scale differentially across species.”

1. While the procedure used to identify transcripts whose expression scale is clearly described, focusing the enrichment on KEGG pathways can only identify metabolic genes that scale. It would be informative and instructive to investigate if and to what extent genes involved in non-metabolic processes, that affect metabolic rates, also scale.

We acknowledge that focusing the enrichment on KEGG pathways does enrich for the identification of metabolic processes that scale. However, we would respectfully submit that because this manuscript focuses on metabolic scaling, this seems to be the most appropriate setting in which to conduct the analysis. New data added in this revision demonstrate that three metabolic enzymes that scaled in the transcriptomics analysis also scale relative to β-actin, further suggesting that the inverse correlation of gene expression with body weight is primarily confined to metabolic processes:

Author Response Figure 3

In addition, we measured the expression of two structural proteins (collagenase 3 [Mmp3] and Larp6) outside of metabolic pathways, relative to β-actin (Actb), and found that neither was differentially expressed relative to actin in mice versus rats:

Author Response Figure 4

We recognize that these data may be confounded by the fact that Actb expression could potentially be different in mice versus rats; however, the fact that metabolic genes scale relative to β-actin (Actb) expression shows that it is unlikely that global mRNA scaling is unlikely to be the sole cause of the metabolic scaling phenotype.

1. The result on flux ratios and absolute fluxes, based on the equations in Table S1, rely on certain assumptions (e.g. metabolic and isotopic steady state, among the others listed in PINTA); the current presentation does not ensure that all assumptions of PINTA are met in the present setting, so the estimates may be biased, leading to alternative explanations for the observed differences in vivo or the lack thereof in vitro.

However, we fully agree with the reviewer that it is critical to ensure that key assumptions are met when presenting tracer data, and thank them for raising this important point. Thus, we have now added data demonstrating that plasma m+1, m+2, and m+7 glucose are in steady state at 100 min of the 120 min in vivo tracer infusion:

Author Response Figure 5

Additionally, we now show that blood glucose and plasma lactate concentrations have reached steady state as well:

Author Response Figure 6

With these data, we validate that the mice and rats are at metabolic and isotopic steady state by the end of the 120 min tracer infusion. We recognize that we have not validated that liver m+1 and m+2 glucose are at steady state, as that would require two additional groups of mice and rats (to sacrifice at 100 and 110 min, compared to the animals euthanized after 120 min of infusion) and introduce additional variability. Additionally, plasma m+1 and m+2 glucose come from endogenous glucose production from 13C tracer, so if m+1 and m+2 glucose are in steady state in plasma, they must be in steady state in liver.

An additional assumption is that liver glycogen is effectively depleted after the overnight fast utilized in these studies. We have now verified this assumption by comparing fed and overnight fasted liver glycogen concentrations, and detect negligible glycogen after the fast in both rats and mice:

Author Response Figure 7

Additionally, we validated isotopic steady state in our hepatocytes incubated in 3-13C lactate. As expected in plated cell studies, cells reached steady state in both [13C] lactate enrichment and m+1 and m+2 glucose enrichment within 60 min. Because net glucose production is measured using the accumulation of glucose, we do not expect – and did not measure – glucose concentration at steady state, but we did confirm that the accumulation of glucose is linear throughout the 6 hr incubation (thus confirming that 6 hr is a reasonable endpoint):

Author Response Figure 8

We very respectfully submit that after 8 prior publications using PINTA called as such (PMID 28986525, 29307489, 29483297, 31545298, 31578240, 32610084, 32132708, 32179679), in addition to several prior publications that utilized PINTA without the acronym, it would not be the most responsible use of animals to try to prove in this manuscript that PINTA is a legitimate means of assessing substrate fluxes in the current manuscript. However, we thank the reviewer for raising the important point regarding assumptions of the method, thereby allowing us to insert data verifying that the key assumptions are met.

1. The findings regarding the flux estimates seem to be fully determined by observed differences in gluconeogenesis (as demonstrated in Fig. 4). Usage of more involved approaches for metabolic flux analysis may provide wider-reaching conclusions beyond selected fluxes that appear fully coupled.

Fluxes are back-calculated from total glucose production so that methodologically they are “coupled”, but this does not mean that glucose production will always mirror other flues. For example, in our 2015 manuscript using PINTA – although we had not yet named the method “PINTA” – we measured decreased endogenous glucose production (EGP) simultaneously with increased citrate synthase flux (mitochondrial oxidation, VTCA, which we have subsequently begun to call VCS in recognition of the fact that different reactions in the TCA cycle can proceed at different rates, but the calculation is the same) (Perry et al. Science 2015).

Similarly, another study demonstrated that the same mitochondrial uncoupler (CRMP) increased VCS while EGP decreased in nonhuman primates (Goedeke et al. Sci. Transl. Med. 2019).

These data demonstrate that, while fluxes are back-calculated from EGP with PINTA, the method is fully capable of detecting differences in oxidative fluxes without, or in the opposite direction of, changes in EGP. We very respectfully submit that we are not aware of what a more “involved” approach for metabolic flux analysis would entail, and that after the 8 prior publications listed in response to the previous point, we are not trying to validate PINTA in the current manuscript.

Reviewer #3 (Public Review):

This manuscript addresses a fundamental aspect of mammalian biology referred to as scaling, in which metabolic processes calibrate to the size of the organism. Longstanding observations related to scaling have been established based on rates of oxygen consumption. This manuscript extends these observations to gene expression and metabolic fluxes in order to discover the metabolic pathways that scale with body mass. The analyses are focused on the liver, which is the metabolic hub of the organism. Gene expression levels gleaned from available databases for organisms of varied sizes are analyzed and queried for scaling based on body mass. This analysis reveals that scaling is mainly a characteristic of metabolic genes. These data inform metabolic flux studies in cultured cells, liver slices and whole organisms. These studies demonstrate that scaling of metabolic fluxes occurs, but not out of the context of the whole organism or intact liver (in the form of liver slices). Scaling of metabolic fluxes is not observed in cultured hepatocytes. Overall, this is an interesting line of inquiry. The data are largely correlative in nature but add important texture to traditional characterization of oxygen consumption rates. The application of flux studies is a particular strength because these reflect the true metabolic processes. Enthusiasm was tempered by certain claims that extend beyond data (e.g., the title that suggests that metabolic scaling applies to tissues other than the liver, which was studied), as well as low numbers of biological replicates in some experiments, studies conducted in a single-gender and a writing style that includes excessive technical jargon.

We thank the reviewer for their time spent evaluating the paper, and for their very helpful comments. We agree that “the application of flux studies is a particular strength because these reflect the true metabolic processes.” We agree that the study was focused on liver, although the previous iteration did include a small amount of white adipose tissue flux data, and have edited the manuscript to make clear that this is a liver-focused manuscript. We have now added specific numbers to each figure legend, and have also added in vivo flux measurements in female rats and mice. Additionally, the manuscript has been edited extensively. We have further detailed these modifications in our point-by-point responses to the reviewer.