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):

This manuscript describes a series of behavioral experiments in which foraging rats are subjected to a novel fear conditioning paradigm. Different groups of animals receive a shock to the dorsal surface of the body paired with either tone, an artificial owl driven forward with pneumatic pressure, or a tone/owl combination. An additional control condition pairs tone with owl alone (ie no shock is delivered). In a subsequent test, only owl+shock and tone/owl+shock animals show increased latency to forage and a withdrawal response to tone (even though owl-shock rats do not experience tone during conditioning). The authors conclude that this tone response is due to sensitization and that fear conditioning does not occur in their experimental setup.

This approach is intriguing and the issues raised by the manuscript are extremely important for the field to consider. However, there are many ways to interpret the results as they stand. One issue of primary importance is whether it can indeed be claimed that conditioning did not readily occur in the tone+shock group. The lack of a particular behavioral conditioned reaction does not equate to an absence of conditioning. It is possible that unseen (i.e. physiological) measures of conditioning, many of which were once standard DVs in the fear conditioning literature, are present in the tone+shock group. This possibility pushes against the claim made in the title and elsewhere. These claims should be softened.

We agree with the reviewer and now acknowledge the following caveat in the discussion (pg. 10): “…although neither the tone-shock group nor the tone-owl group showed overt manifestations of fear conditioning (as measured by fleeing or freezing) to the tone that prevented a successful procurement of food, the possibility of physiological (e.g., cardiovascular, respiratory) changes associated with tone-induced fear (Steimer, 2002) cannot be excluded in these animals…”

Because systemic, group-level retreat CRs are not noted in the tone+shock condition, it would indeed be important to establish if there are any experimental circumstances in which tone paired with a US applied to the dorsal surface of the body can produce consistent reactions (e.g. freezing) to tone alone. Though it may seem likely that tone + dorsal shock would indeed produce freezing in a different setting, this result should not be taken for granted - we've known since the 'noisy water' experiment (Garcia & Koelling, 1966) that not every CS pairs with every US and that association can indeed be selective. A positive control would be clarifying. If the authors could demonstrate that tone+dorsal shock produces freezing to tone in a commonly used fear conditioning setup (ie standard cubicle chamber) then the lack of a retreat CR in their naturalistic paradigm would gain added meaning.

This is an excellent suggestion. As recommended, we performed a positive control experiment where naïve rats that underwent the same subcutaneous wire implant surgery were placed in a standard experimental chamber and presented with a delayed tone-shock pairing (same tone frequency/intensity and shock intensity/duration; the 24.1 s CS duration was based on the mean CS duration of tone-shock animals in the naturalistic fear conditioning experiment). As can be seen in Author response image 1 (Figure 4 in the revised manuscript) below, these animals exhibited reliable postshock freezing in a conditioning chamber (fear conditioning day 1) and tone CS-evoked freezing in a novel chamber (tone testing day 2), indicating that our original finding (i.e., no evidence of auditory and contextual fear conditioning in an ecologically-relevant environment) is unlikely due to a dorsal neck/body shock US per se.

Author response image 1. Auditory fear conditioning in a standard experimental chamber. (A) Illustrations of a rat implanted with wires subcutaneously in the dorsal neck/body region undergoing successive days of habituation (10 min tethered, conditioning chamber), training (a single tone CS-shock US pairing), and tone testing (context shift). (B) Mean (crimson line) and individual (gray lines) percent freezing data from 8 rats (4 females, 4 males) during training in context A: 3 min baseline (BL1, BL2, BL3); 23.1 s epoch of tone (T) excluding 1 s overlap with shock (S); 1 min postshock (PS). (C) Mean and individual percent freezing data during tone testing in context B: 1 min baseline (BL1); 3 min tone (T1, T2, T3); 1 min post-tone (PT). (D) Mean + SEM (bar) and individual (dots) percent freezing to tone CS before (Train, T) and after (Test, T1) undergoing auditory fear conditioning (paired t-test; t(7) = -3.163, p = 0.016). * p < 0.05

The altered withdrawal trajectory seen in owl+shock and tone/owl+shock groups occurs in neither the tone+shock nor the tone+owl group, introducing the possibility that it results from the specific pairing of owl and shock. Put differently - this response may indeed by an associative CR. Do altered withdrawal angles persist if animals that receive owl+shock are exposed to owl again the next day? Do manipulations of the owl and shock that diminish fear conditioning (e.g. unpairing of owl and shock stimuli) eliminate deflected withdrawal angles when the subject is exposed to owl alone? If so, it would cut against the interpretation that fear conditioning does not occur in the setup described here, and would instead demonstrate that it is indeed central to predatory defense. This interpretation is compatible with the effect of hippocampal lesion on freezing evoked by a live predator. Destruction of the rat hippocampus diminishes cat-evoked freezing - this is thought to occur because the rapid association of the cat's various features with threatening action is not formed by the rat (Fanselow, 2000, 2018). Even though this interpretation of the results differs from the authors', it in no way diminishes the interest of this work. This paradigm may indeed be a novel means by which to study rapidly acquired associations with ethological relevance. Follow-up experiments of the type described above are necessary to disambiguate opposing views of the current dataset.

Whether “altered withdrawal angles persist if animals that receive owl+shock [a US-US pairing] are exposed to owl again the next day” is an interesting question, as it is conceivable that the owl US (Zambetti et al., 2019, iScience) can function as a CS to evoke anticipatory characteristic of the conditioned fear. This possibility is now mentioned as a caveat (pg. 10): “…the erratic escape trajectory behavior exhibited by owl-shock and tone/owl-shock animals may be indicative of rapid associative processes at work (Fanselow 2018). For example, the immediate-shock (and delayed shock-context shift) deficit in freezing (e.g., Fanselow 1986; Landeira-Fernandez et al., 2006) provides compelling evidence that postshock freezing is not a UR but rather a CR to the contextual representation CS that rapidly became associated with the footshock US. In a similar vein then the erratic escape CR topography in owl-shock and tone/owl-shock animals might represent a shift in ‘functional CR topography’ (Fanselow & Wassum 2016) resulting from the rapid association between some salient features of the owl and the dorsal neck/body shock. A rapid owl-shock association nevertheless cannot explain the owl-shock animals’ subsequent fleeing behavior to a novel tone (in the absence of owl), which likely reflects nonassociative fear.”

Reviewer #2 (Public Review):

This work is dealing with an interesting question whether a simple, one trial CS+US (Pavlovian) association occurs in a naturalistic environment. Pavlovian fear conditioning contains a repetition of a neutral sensory signal (tone, CS) which is paired with a mild US, usually foot-shock (<1 mA; thus, unpleasant rather than painful) and the CS+US association drives associative learning. In this paper, a single 2.5 mA electrical shock was paired with a novel 80 dB tone to monitor the occurrence of learning via measuring success rate and latency of foraging for food. Some animals experienced an owl-looming matched with the US, just before reaching the food. The authors placed hunger-motivated rats into a custom-built arena equipped with safe nest, gate, food zone as well as with a delivery of a self-controlled US (electrical shock in the neck muscle and/or owl-looming). The US was activated by the rats by approaching to the food. Thus, a conflicting situation was provoked where procuring the food is paired with an aversive conditioned signal. Four groups of rats were included in the experiments based on their conditioning types: tone+ shock, tone+ shock+ owl, shock+owl and tone+owl. Due to these conditioning procedures, none of the rat procured the food but fled to the nest. In contrast, in the retrieval phases (next two days), the tone-shock and tone-owl groups successfully procured the pellets but not the tone-shock-owl group during the conditioned tone presentation. Rats in the latter group fled to the nest upon tone presentation at the food zone. As the shock-owl animals (conditioned without tone) also fled to the nest triggered by (unfamiliar) tone presentation, their and the tone+shock+owl group's fled responses were assigned to be non-associative sensitization-like process. Furthermore, during the pre-tone trials, all groups showed similar behavior as in the tone test. These findings led the authors to conclude that classical Pavlovian fear conditioning may not present in an ecologically relevant environment.

The raised question is relevant for broad audience of neuroscience and behavioral scientist. However, as the used fear conditioning paradigm is not a common one, it is difficult to interpret the finding. It is based on a single pairing of an unfamiliar, salient tone with a very strong (traumatizing?) electrical shock, delivered directly into the neck muscle and an innate signal (owl looming). In addition, as the tone presentation was followed by many events (gate opening, presence of food, shock and/or owl-looming) in front of the animals, it is hard to image what sort of tone association could be formed at all.

We thank the reviewer for mentioning several important considerations. In regards to the shock amplitude used here, fear conditioning studies in rats have employed a wide range of numbers, durations and intensities of footshock; e.g., three footshocks: 1.0 mA/0.75-s and 4.0 mA/3-s (Fanselow 1984), 75 footshocks: 1 mA/2-s (Maren 1999; Zimmerman et al. 2007). Note also that 16-20 periorbital shocks (2.0 mA, 8 pulse train at 5 Hz) have been used in auditory fear conditioning in rats (Moita et al. 2003; Blair et al. 2005). Thus, it is unlikely that a single 2.5 mA dorsal neck/body shock (subcutaneous and not in the neck muscle) used in the present study is particularly traumatizing compared to higher intensity/longer duration (e.g., 4.0 mA/3-s) and far more numerous (e.g., 75) footshocks employed in fear conditioning studies.

The relationship between footshock intensity and fear conditioning also warrants further discussion. Sigmundi, Bouton, and Bolles (1980) examined conditioned freezing in rats to 15 footshocks of 0.5, 1.0 and 2.0 mA intensities (0.5-s duration) and found that “[tone] CS-evoked freezing increased with US intensity.” In contrast, Fanselow (1984) observed relatively higher contextual freezing in rats subjected to three bouts of 1.0 mA/0.75-s than 4 mA/3-s footshocks. Irrespective, the animals that received three 4 mA/3-s footshocks still exhibited robust freezing. Based on the positive control experimental results (see above), it is unlikely that the present study’s failure to observe conditioned fear is due to the use of 2.5 mA shock intensity.

As the animals in the present study underwent 5 baseline days of foraging (3 trials per day), they would have been habituated to the computer-controlled automated gate opening-closing and the presence of food by the time of tone-shock, tone-owl, owl-shock and tone-owl/shock events, making it unlikely that the tone would associate with the gate/food stimuli. In the employed delay conditioning configuration, the tone CS has greater temporal contiguity with the US (shock and/or owl) and the US is both novel and surprising relative to the other stimuli in the arena environment. Thus, it is more plausible that the tone CS would be associated with the intended US. In summary, we believe that if fear conditioning necessitates relatively sterile environmental settings in order to transpire, then fear conditioning would be implausible in the natural world filled with dynamic, complex stimuli.

One could also argue that if a hungry animal does not try to collect food after an unpleasant, even a painful experience, then, it normally dies soon (thus, that is not a 'natural' behavior). The tone+shock and tone+owl groups showed similar behavioral features throughout the entire experiments and may reconcile the natural events: although these rats had had negative experience before, were still approaching to food zone due their hunger. Because of their motivation for food, the authors concluded that no association was formed. Based on this single measure, is it right to do so?

In nature, prey animals adjust their foraging behavior to minimize danger (e.g., Stephens and Krebs 1986 Foraging Theory; Lima and Dill 1990 Can J Zool); thus, it is improbable that an aversive experience will lead to end of food seeking behavior leading to death. Indeed, Choi and Kim (2010 Proc Natl Acad Sci) employed a similar seminaturalistic environment (as the present study) and found that rats adjust their foraging behavior as a function of the predatory threat distance, consistent with the “predatory imminence” model (Fanselow and Lester 1988). Since only behavioral measures of fear were assessed (i.e., fleeing, latency to enter forage zone, pellet procurement), we now acknowledge a caveat in the discussion (see response to Reviewer 1’s comment 1). Note, however, that unlike the tone-shock paired animals that failed to flee to the tone CS and successfully procured the food pellet, the owl-shock animals exhibited robust fear behavior (promptly fled, ceasing foraging) to a novel tone.

Reviewer #3 (Public Review):

In this study, the authors aimed to test whether rats could be fear conditioned by pairing a subdermal electric shock to a tone, an owl-like approaching stimulus, or a combination of these in a naturalistic-like environment. The authors designed a task in which rats foraging for food were exposed to a tone paired to a shock, an owl-like stimulus, a combination of the owl and the shock, or paired the owl to a shock in a single trial. The authors indexed behaviors related to food approach after conditioning. The authors found that animals exposed to the owl-shock or the tone/owl-shock pairing displayed a higher latency to approach the food reward compared to animals that were presented with the tone-shock or the tone-owl pairing. These results suggest that pairing the owl with the shock was sufficient to induce inhibitory avoidance, whereas a single pairing of the tone-shock or the tone-owl was not. The authors concluded that standard fear conditioning does not readily occur in a naturalistic-like environment and that the inhibitory avoidance induced by the owl-shock pairing could be the result of increased sensitization rather than a fear association.

Strengths:

The manuscript is well-written, the behavioral assay is innovative, and the results are interesting. The inclusion of both males and females, and the behavioral sex comparison was commendable. The findings are timely and would be highly relevant to the field.

Weaknesses:

However, in its current state, this study does not provide convincing evidence to support their main claim that Pavlovian fear conditioning does not readily occur in naturalistic environments. The innovative task presented in this study is more akin to an inhibitory avoidance task rather than fear conditioning and should be reframed in such way.

The reviewer’s comment is theoretically important in translating laboratory studies of fear to real world situations. Because our animals were engaged in a purposive/goal-oriented foraging behavior, that is, the leaving of nest in search of food in an open space brought about tone-shock, tone-owl, owl-shock and tone/owl shock outcomes, one can make the case that this is in principle an inhibitory avoidance (instrumental fear conditioning) task rather than a Pavlovian fear conditioning task. A pertinent question then is whether procedurally ‘pure’ laboratory Pavlovian conditioning tasks (i.e., displacing animals from their home cage to an experimental chamber and presenting CS and US) are possible in real world settings where behaviors of animals and humans are largely purposive/goal-oriented (Tolman 1948 Psychol Rev). It is generally accepted that “Outside the laboratory, stimulus [Pavlovian] learning and response [Instrumental] learning are almost inseparable (Bouton 2007 Learning and Behavior, pg. 28).” The goal of our study was to investigate whether widely-employed auditory fear conditioning readily produces associative fear memory that guides future behavior in animals performing naturalistic foraging behavior, and insofar as presenting a salient tone CS followed by an aversive shock US, the present study has a Pavlovian fear component.

We thank the reviewer for raising this concern and have addressed the Pavlovian vs. Instrumental fear conditioning aspects of our study in the revised manuscript (pg. 10): “…there are obvious procedural differences between standard fear conditioning versus naturalistic fear conditioning. In the former paradigm, typically ad libitum fed animals are placed in an experimental chamber for a fixed time before receiving a CS-US pairing (irrespective of their ongoing behavior). Thus, the CS duration and ISI are constant across subjects. In our study, hunger-motivated rats searching for food must navigate to a fixed location in a large arena before experiencing a CS-US pairing (instrumental- or response-contingent). Because animals approach the US trigger zone at different latencies, the CS duration and ISI are variable across subjects.”

References

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Author Response:

Reviewer #1 (Public Review):

Overview

This is a well-conducted study and speaks to an interesting finding in an important topic, whether ethological validity causes co-variation in gamma above and beyond the already present ethological differences present in systemic stimulus sensitivity.

I like the fact that while this finding (seeing red = ethnologically valid = more gamma) seems to favor views the PI has argued for, the paper comes to a much simpler and more mechanistic conclusion. In short, it's good science.

I think they missed a key logical point of analysis, in failing to dive into ERF <----> gamma relationships. In contrast to the modeled assumption that they have succeeded in color matching to create matched LGN output, the ERF and its distinct features are metrics of afferent drive in their own data. And, their data seem to suggest these two variables are not tightly correlated, so at very least it is a topic that needs treatment and clarity as discussed below.

Further ERF analyses are detailed below.

Minor concerns

In generally, very well motived and described, a few terms need more precision (speedily and staircased are too inaccurate given their precise psychophysical goals)

We have revised the results to clarify:

"For colored disks, the change was a small decrement in color contrast, for gratings a small decrement in luminance contrast. In both cases, the decrement was continuously QUEST-staircased (Watson and Pelli, 1983) per participant and color/grating to 85% correct detection performance. Subjects then reported the side of the contrast decrement relative to the fixation spot as fast as possible (max. 1 s), using a button press."

The resulting reaction times are reported slightly later in the results section.

I got confused some about the across-group gamma analysis:

"The induced change spectra were fit per participant and stimulus with the sum of a linear slope and up to two Gaussians." What is the linear slope?

The slope is used as the null model – we only regarded gamma peaks as significant if they explained spectrum variance beyond any linear offsets in the change spectra. We have clarified in the Results:

"To test for the existence of gamma peaks, we fit the per-participant, per-stimulus change spectra with three models: a) the sum of two gaussians and a linear slope, b) the sum of one Gaussian and a linear slope and c) only a linear slope (without any peaks) and chose the best-fitting model using adjusted R2-values."

To me, a few other analyses approaches would have been intuitive. First, before averaging peak-aligned data, might consider transforming into log, and might consider making average data with measures that don't confound peak height and frequency spread (e.g., using the FWHM/peak power as your shape for each, then averaging).

The reviewer comments on averaging peak-aligned data. This had been done specifically in Fig. 3C. Correspondingly, we understood the reviewer’s suggestion as a modification of that analysis that we now undertook, with the following steps: 1) Log-transform the power-change values; we did this by transforming into dB; 2) Derive FWHM and peak power values per participant, and then average those; we did this by a) fitting Gaussians to the per-participant, per-stimulus power change spectra, b) quantifiying FWHM as the Gaussian’s Standard Deviation, and the peak power as the Gaussian’s amplitude; 3) average those parameters over subjects, and display the resulting Gaussians. The resulting Gaussians are now shown in the new panel A in Figure 3-figure supplement 1.

(A) Per-participant, the induced gamma power change peak in dB was fitted with a Gaussian added to an offset (for full description, see Methods). Plotted is the resulting Gaussian, with peak power and variance averaged over participants.

Results seem to be broadly consistent with Fig. 3C.

Moderate

I. I would like to see a more precise treatment of ERF and gamma power. The initial slope of the ERF should, by typical convention, correlate strongly with input strength, and the peak should similarly be a predictor of such drive, albeit a weaker one. Figure 4C looks good, but I'm totally confused about what this is showing. If drive = gamma in color space, then these ERF features and gamma power should (by Occham's sledgehammer…) be correlated. I invoke the sledgehammer not the razor because I could easily be wrong, but if you could unpack this relationship convincingly, this would be a far stronger foundation for the 'equalized for drive, gamma doesn't change across colors' argument…(see also IIB below)…

…and, in my own squinting, there is a difference (~25%) in the evoked dipole amplitudes for the vertically aligned opponent pairs of red- and green (along the L-M axis Fig 2C) on which much hinges in this paper, but no difference in gamma power for these pairs. How is that possible? This logic doesn't support the main prediction that drive matched differences = matched gamma…Again, I'm happy to be wrong, but I would to see this analyzed and explained intuitively.

As suggested by the reviewer, we have delved deeper into ERF analyses. Firstly, we overhauled our ERF analysis to extract per-color ERF shape measures (such as timing and slope), added them as panels A and B in Figure 2-figure supplement 1:

Figure 2-figure supplement 1. ERF and reaction time results: (A) Average pre-peak slope of the N70 ERF component (extracted from 2-12 ms before per-color, per-participant peak time) for all colors. (B) Average peak time of the N70 ERF component for all colors. […]. For panels A-C, error bars represent 95% CIs over participants, bar orientation represents stimulus orientation in DKL space. The length of the scale bar corresponds to the distance from the edge of the hexagon to the outer ring.

We have revised the results to report those analyses:

"The initial ERF slope is sometimes used to estimate feedforward drive. We extracted the per-participant, per-color N70 initial slope and found significant differences over hues (F(4.89, 141.68) = 7.53, pGG < 410 6). Specifically, it was shallower for blue hues compared to all other hues except for green and green-blue (all pHolm < 710-4), while it was not significantly different between all other stimulus hue pairs (all pHolm > 0.07, Figure 2-figure supplement 1A), demonstrating that stimulus drive (as estimated by ERF slope) was approximately equalized over all hues but blue.

The peak time of the N70 component was significantly later for blue stimuli (Mean = 88.6 ms, CI95% = [84.9 ms, 92.1 ms]) compared to all (all pHolm < 0.02) but yellow, green and green-yellow stimuli, for yellow (Mean = 84.4 ms, CI95% = [81.6 ms, 87.6 ms]) compared to red and red-blue stimuli (all pHolm < 0.03), and fastest for red stimuli (Mean = 77.9 ms, CI95% = [74.5 ms, 81.1 ms]) showing a general pattern of slower N70 peaks for stimuli on the S-(L+M) axis, especially for blue (Figure 2-figure supplement 1B)."

We also checked if our main findings (equivalence of drive-controlled red and green stimuli, weaker responses for S+ stimuli) are robust when controlled for differences in ERF parameters and added in the Results:

"To attempt to control for potential remaining differences in input drive that the DKL normalization missed, we regressed out per-participant, per-color, the N70 slope and amplitude from the induced gamma power. Results remained equivalent along the L-M axis: The induced gamma power change residuals were not statistically different between red and green stimuli (Red: 8.22, CI95% = [-0.42, 16.85], Green: 12.09, CI95% = [5.44, 18.75], t(29) = 1.35, pHolm = 1.0, BF01 = 3.00).

As we found differences in initial ERF slope especially for blue stimuli, we checked if this was sufficient to explain weaker induced gamma power for blue stimuli. While blue stimuli still showed weaker gamma-power change residuals than yellow stimuli (Blue: -11.23, CI95% = [-16.89, -5.57], Yellow: -6.35, CI95% = [-11.20, -1.50]), this difference did not reach significance when regressing out changes in N70 slope and amplitude (t(29) = 1.65, pHolm = 0.88). This suggests that lower levels of input drive generated by equicontrast blue versus yellow stimuli might explain the weaker gamma oscillations induced by them."

We added accordingly in the Discussion:

"The fact that controlling for N70 amplitude and slope strongly diminished the recorded differences in induced gamma power between S+ and S- stimuli supports the idea that the recorded differences in induced gamma power over the S-(L+M) axis might be due to pure S+ stimuli generating weaker input drive to V1 compared to DKL-equicontrast S- stimuli, even when cone contrasts are equalized.."

Additionally, we made the correlation between ERF amplitude and induced gamma power clearer to read by correlating them directly. Accordingly, the relevant paragraph in the results now reads:

"In addition, there were significant correlations between the N70 ERF component and induced gamma power: The extracted N70 amplitude was correlated across colors with the induced gamma power change within participants with on average r = -0.38 (CI95% = [-0.49, -0.28], pWilcoxon < 4*10-6). This correlation was specific to the gamma band and the N70 component: Across colors, there were significant correlation clusters between V1 dipole moment 68-79 ms post-stimulus onset and induced power between 28 54 Hz and 72 Hz (Figure 4C, rmax = 0.30, pTmax < 0.05, corrected for multiple comparisons across time and frequency)."

II. As indicated above, the paper rests on accurate modeling of human LGN recruitment, based in fact on human cone recruitment. However, the exact details of how such matching was obtained were rapidly discussed-this technical detail is much more than just a detail in a study on color matching: I am not against the logic nor do I know of a flaw, but it's the hinge of the paper and is dealt with glancingly.

A. Some discussion of model limitations

B. Why it's valid to assume LGN matching has been achieved using data from the periphery: To buy knowledge, nobody has ever recorded single units in human LGN with these color stimuli…in contrast, the ERF is 'in their hands' and could be directly related (or not) to gamma and to the color matching predictions of their model.

We have revised the respective paragraph of the introduction to read:

"Earlier work has established in the non-human primate that LGN responses to color stimuli can be well explained by measuring retinal cone absorption spectra and constructing the following cone-contrast axes: L+M (capturing luminance), L-M (capturing redness vs. greenness), and S-(L+M) (capturing S-cone activation, which correspond to violet vs. yellow hues). These axes span a color space referred to as DKL space (Derrington, Krauskopf, and Lennie, 1984). This insight can be translated to humans (for recent examples, see Olkkonen et al., 2008; Witzel and Gegenfurtner, 2018), if one assumes that human LGN responses have a similar dependence on human cone responses. Recordings of human LGN single units to colored stimuli are not available (to our knowledge). Yet, sensitivity spectra of human retinal cones have been determined by a number of approaches, including ex-vivo retinal unit recordings (Schnapf et al., 1987), and psychophysical color matching (Stockman and Sharpe, 2000). These human cone sensitivity spectra, together with the mentioned assumption, allow to determine a DKL space for human observers. To show color stimuli in coordinates that model LGN activation (and thereby V1 input), monitor light emission spectra for colored stimuli can be measured to define the strength of S-, M-, and L-cone excitation they induce. Then, stimuli and stimulus background can be picked from an equiluminance plane in DKL space. "

Reviewer #2 (Public Review):

The major strengths of this study are the use of MEG measurements to obtain spatially resolved estimates of gamma rhythms from a large(ish) sample of human participants, during presentation of stimuli that are generally well matched for cone contrast. Responses were obtained using a 10deg diameter uniform field presented in and around the centre of gaze. The authors find that stimuli with equivalent cone contrast in L-M axis generated equivalent gamma - ie. that 'red' (+L-M) stimuli do not generate stronger responses than 'green (-L+M). The MEG measurements are carefully made and participants performed a decrement-detection task away from the centre of gaze (but within the stimulus), allowing measurements of perceptual performance and in addition controlling attention.

There are a number of additional observations that make clear that the color and contrast of stimuli are important in understanding gamma. Psychophysical performance was worst for stimuli modulated along the +S-(L+M) direction, and these directions also evoked weakest evoked potentials and induced gamma. There also appear to be additional physiological asymmetries along non-cardinal color directions (e.g. Fig 2C, Fig 3E). The asymmetries between non-cardinal stimuli may parallel those seen in other physiological and perceptual studies and could be drawn out (e.g. Danilova and Mollon, Journal of Vision 2010; Goddard et al., Journal of Vision 2010; Lafer-Sousa et al., JOSA 2012).

We thank the review for the pointers to relevant literature and have added in the Discussion:

"Concerning off-axis colors (red-blue, green-blue, green-yellow and red-yellow), we found stronger gamma power and ERF N70 responses to stimuli along the green-yellow/red-blue axis (which has been called lime-magenta in previous studies) compared to stimuli along the red-yellow/green-blue axis (orange-cyan). In human studies varying color contrast along these axes, lime-magenta has also been found to induce stronger fMRI responses (Goddard et al., 2010; but see Lafer-Sousa et al., 2012), and psychophysical work has proposed a cortical color channel along this axis (Danilova and Mollon, 2010; but see Witzel and Gegenfurtner, 2013)."

Similarly, the asymmetry between +S and -S modulation is striking and need better explanation within the model (that thalamic input strength predicts gamma strength) given that +S inputs to cortex appear to be, if anything, stronger than -S inputs (e.g. DeValois et al. PNAS 2000).

We followed the reviewer’s suggestion and modified the Discussion to read:

"Contrary to the unified pathway for L-M activation, stimuli high and low on the S-(L+M) axis (S+ and S ) each target different cell populations in the LGN, and different cortical layers within V1 (Chatterjee and Callaway, 2003; De Valois et al., 2000), whereby the S+ pathway shows higher LGN neuron and V1 afferent input numbers (Chatterjee and Callaway, 2003). Other metrics of V1 activation, such as ERPs/ERFs, reveal that these more numerous S+ inputs result in a weaker evoked potential that also shows a longer latency (our data; Nunez et al., 2021). The origin of this dissociation might lie in different input timing or less cortical amplification, but remains unclear so far. Interestingly, our results suggest that cortical gamma is more closely related to the processes reflected in the ERP/ERF: Stimuli inducing stronger ERF induced stronger gamma; and controlling for ERF-based measures of input drives abolished differences between S+ and S- stimuli in our data."

Given that this asymmetry presents a potential exception to the direct association between LGN drive and V1 gamma power, we have toned down claims of a direct input drive to gamma power relationship in the Title and text and have refocused instead on L-M contrast.

My only real concern is that the authors use a precomputed DKL color space for all observers. The problem with this approach is that the isoluminant plane of DKL color space is predicated on a particular balance of L- and M-cones to Vlambda, and individuals can show substantial variability of the angle of the isoluminant plane in DKL space (e.g. He, Cruz and Eskew, Journal of Vision 2020). There is a non-negligible chance that all the responses to colored stimuli may therefore be predicted by projection of the stimuli onto each individual's idiosyncratic Vlambda (that is, the residual luminance contrast in the stimulus). While this would be exhaustive to assess in the MEG measurements, it may be possible to assess perceptually as in the He paper above or by similar methods. Regardless, the authors should consider the implications - this is important because, for example, it may suggest that important of signals from magnocellular pathway, which are thought to be important for Vlambda.

We followed the suggestion of the reviewer, performed additional analyses and report the new results in the following Results text:

"When perceptual (instead of neuronal) definitions of equiluminance are used, there is substantial between-subject variability in the ratio of relative L- and M-cone contributions to perceived luminance, with a mean ratio of L/M luminance contributions of 1.5-2.3 (He et al., 2020). Our perceptual results are consistent with that: We had determined the color-contrast change-detection threshold per color; We used the inverse of this threshold as a metric of color change-detection performance; The ratio of this performance metric between red and green (L divided by M) had an average value of 1.48, with substantial variability over subjects (CI95% = [1.33, 1.66]).

If such variability also affected the neuronal ERF and gamma power measures reported here, L/M-ratios in color-contrast change-detection thresholds should be correlated across subjects with L/M-ratios in ERF amplitude and induced gamma power. This was not the case: Change-detection threshold red/green ratios were neither correlated with ERF N70 amplitude red/green ratios (ρ = 0.09, p = 0.65), nor with induced gamma power red/green ratios (ρ = -0.17, p = 0.38)."

Reviewer #3 (Public Review):

This is an interesting article studying human color perception using MEG. The specific aim was to study differences in color perception related to different S-, M-, and L-cone excitation levels and especially whether red color is perceived differentially to other colors. To my knowledge, this is the first study of its kind and as such very interesting. The methods are excellent and manuscript is well written as expected this manuscript coming from this lab. However, illustrations of the results is not optimal and could be enhanced.

Major

The results presented in the manuscript are very interesting, but not presented comprehensively to evaluate the validity of the results. The main results of the manuscript are that the gamma-band responses to stimuli with absolute L-M contrast i.e. green and red stimuli do not differ, but they differ for stimuli on the S-(L+M) (blue vs red-green) axis and gamma-band responses for blue stimuli are smaller. These data are presented in figure 3, but in it's current form, these results are not well conveyed by the figure. The main results are illustrated in figures 3BC, which show the average waveforms for grating and for different color stimuli. While there are confidence limits for the gamma-band responses for the grating stimuli, there are no confidence limits for the responses to different color stimuli. Therefore, the main results of the similarities / differences between the responses to different colors can't be evaluated based on the figure and hence confidence limits should be added to these data.

Figure 3E reports the gamma-power change values after alignment to the individual peak gamma frequencies, i.e. the values used for statistics, and does report confidence intervals. Yet, we see the point of the reviewer that confidence intervals are also helpful in the non-aligned/complete spectra. We found that inclusion of confidence intervals into Figure 3B,C, with the many overlapping spectra, renders those panels un-readable. Therefore, we included the new panel Figure 3-figure supplement 2A, showing each color’s spectrum separately:

(A) Per-color average induced power change spectra. Banding shows 95% confidence intervals over participants. Note that the y-axis varies between colors.

It is also not clear from the figure legend, from which time-window data is averaged for the waveforms.

We have added in the legend:

"All panels show power change 0.3 s to 1.3 s after stimulus onset, relative to baseline."

The time-resolved profile of gamma-power changes are illustrated in Fig. 3D. This figure would a perfect place to illustrate the main results. However, of all color stimuli, these TFRs are shown only for the green stimuli, not for the red-green differences nor for blue stimuli for which responses were smaller. Why these TFRs are not showed for all color stimuli and for their differences?

Figure 3-figure supplement 3. Per-color time-frequency responses: Average stimulus-induced power change in V1 as a function of time and frequency, plotted for each frequency.

We agree with the reviewer that TFR plots can be very informative. We followed their request and included TFRs for each color as Figure 3-Figure supplement 3.

Regarding the suggestion to also include TFRs for the differences between colors, we note that this would amount to 28 TFRs, one each for all color combinations. Furthermore, while gamma peaks were often clear, their peak frequencies varied substantially across subjects and colors. Therefore, we based our statistical analysis on the power at the peak frequencies, corresponding to peak-aligned spectra (Fig. 3c). A comparison of Figure 3C with Figure 3B shows that the shape of non-aligned average spectra is strongly affected by inter-subject peak-frequency variability and thereby hard to interpret. Therefore, we refrained from showing TFR for differences between colors, which would also lack the required peak alignment.

Author Response:

Reviewer #1:

Insulin-secreting beta-cells are electrically excitable, and action potential firing in these cells leads to an increase in the cytoplasmic calcium concentration that in turn stimulates insulin release. Beta-cells are electrically coupled to their neighbours and electrical activity and calcium waves are synchronised across the pancreatic islets. How these oscillations are initiated are not known. In this study, the authors identify a subset of 'first responders' beta-cells that are the first to respond to glucose and that initiate a propagating Ca2+ wave across the islet. These cells may be particularly responsive because of their intrinsic electrophysiological properties. Somewhat unexpectedly, the electrical coupling of first responder cells appears weaker than that in the other islet cells but this paradox is well explained by the authors. Finally, the authors provide evidence of a hierarchy of beta-cells within the islets and that if the first responder cells are destroyed, other islet cells are ready to take over.

The strengths of the paper are the advanced calcium imaging, the photoablation experiments and the longitudinal measurements (up to 48h).

Whilst I find the evidence for the existence of first responders and hierarchy convincing, the link between the first responders in isolated individual islets and first phase insulin secretion seen in vivo (which becomes impaired in type-2 diabetes) seems somewhat overstated. It is is difficult to see how first responders in an islet can synchronise secretion from 1000s (rodents) to millions of islets (man) and it might be wise to down-tone this particular aspect.

We thank the reviewer for highlighting this point. We acknowledge that we did not measure insulin from individual islets post first responder cell ablation, where we observed diminished first phase Ca2+. We do note that studies have linked the first phase Ca2+ response to first phase insulin release [Henquin et al, Diabetes (2006) and Head et al, Diabetes (2012)], albeit with additional amplification signals for higher glucose elevations. Thus a diminished first phase Ca2+ would imply a diminished first phase insulin (although given the amplifying signals the converse would not necessarily be the case).

Nevertheless there are also important caveats to our experiment. Within islets we ablated a single first responder cell. In small islets this ablation diminished Ca2+ in the plane that we imaged. In larger islets this ablation did not, pointing to the presence of multiple first responder cells. Furthermore we only observed the plane of the islet containing the ablated first responder. It is possible elsewhere in the islet that [Ca2+] was not significantly disrupted. Thus even within a small islet it is possible for redundancy, where multiple first responder cells are present and that together drive first phase [Ca2+] across the islet. Loss of a single first responder cell only disrupts Ca2+ locally. That we see a relationship between the timing of the [Ca2+] response and distance from the first responder would support this notion. Results from the islet model also support this notion, where >10% of cells were required to be ablate to significantly disrupt first-phase Ca2+.

While we already discuss the issue of redundancy in large islets and in 3D, we now briefly mention the importance of measuring insulin release.

Reviewer #2:

Kravets et al. further explored the functional heterogeneity in insulin-secreting beta cells in isolated mouse islets. They used slow cytosolic calcium [Ca2+] oscillations with a cycle period of 2 to several minutes in both phases of glucose-dependent beta cell activity that got triggered by a switch from unphysiologically low (2 mM) to unphysiologically high (11 mM) glucose concentration. Based on the presented evidence, they described a distinct population of beta cells responsible for driving the first phase [Ca2+] elevation and characterised it to be different from some other previously described functional subpopulations.

Strengths:

The study uses advanced experimental approaches to address a specific role a subpopulation of beta cells plays during the first phase of an islet response to 11 mM glucose or strong secretagogues like glibenclamide. It finds elements of a broadscale complex network on the events of the slow time scale [Ca2+] oscillations. For this, they appropriately discuss the presence of most connected cells (network hubs) also in slower [Ca2+] oscillations.

Weakness:

The critical weakness of the paper is the evaluation of linear regressions that should support the impact of relative proximity (Fig. 1E), of the response consistency (Fig. 2C), and of increased excitability of the first responder cells (Fig. 3B). None of the datasets provided in the submission satisfies the criterion of normality of the distribution of regression residuals. In addition, the interpretation that the majority of first responder cells retain their early response time could as well be interpreted that the majority does not.

We thank the reviewers for their input, as it really opened multiple opportunities for us to improve our analysis and strengthen our arguments of the existence and consistency of the first responder cells. We present more detailed analysis for these respective figures below and describe how these are included in the manuscript.

As it is described below, we performed additional in-depth analysis and statistical evaluation of the data presented in figures 1E, 2C, and 3B. We now report that two of the datasets (Fig.1 E, Fig.2 C) satisfy the criterion of normality of the distribution of regression residuals. The third dataset (Fig.3 B) does not satisfy this criterion, and we update our interpretation of this data in the text.

Figure 1E Statistics, Scatter: We now show the slope and p-value indicating deviation of the slope from 0, and r^2 values in Fig.1 E. While the scatter is large (r^2=0.1549 in Fig.1E) for cells located at all distances from the first responder cell, we found that scatter substantially diminishes when we consider cells located closer to the first responder (r^2=0.3219 in Fig.S1 F): the response time for cells at distances up to 60 μm from the first responder cells now is shown in Fig.S1 F. The choice of 60 μm comes from it being the maximum first-to-last responder distance in our data set (see red box in Fig.1D).

Additionally, we noticed that within larger islets there may be multiple domains with their own first responder in the center (now in Fig.S1 E) and below. Linear distance/time dependence is preserved withing each domain.

Figure 1E Normality of residuals: We appreciate reviewer’s suggestion and now see that the original “distance vs time” dependence in Fig.1 E did not meet normality of residuals test. When plotted as distance (μm)/response time (percentile), the cumulative distribution still did not meet the Shapiro-Wilk test for normality of residuals (see QQ plot “All distances” below). However, for cells located in the 60 μm proximity of the first responder, the residuals pass the Shapiro- Wilk normality test. The QQ-plots for “up to 60 μm distances” are included in Fig.S1 G.

Figure 2C Statistic and Scatter: After consulting a biostatistician (Dr. Laura Pyle), we realized that since the Response time during initial vs repeated glucose elevation was measured in the same islet, these were repeated measurements on the same statistical units (i.e. a longitudinal study). Therefore, it required a mixed model analysis, as opposed to simple linear regression which we used initially. We now have applied linear mixed effects model (LMEM) to LN- transformed (original data + 0.0001). The 0.0001 value was added to avoid issues of LN(0).

We now show LMEM-derived slope and p-value indicating deviation of the slope from 0 in Fig.2 C. Further, we performed sorting of the data presented in Fig.2 C by distance to each of the first responders (now added to Fig.2D). An example of the sorted vs non-sorted time of response in the large islet with multiple first responders is added to the Source Data – Figure 1. We found a substantial improvement of the scatter in the distance- sorted data, compared to the non-sorted, which indicates that consistency of the glucose response of a cell correlates with it’s proximity to the first responder. We also discuss this in the first sub-section of the Discussion.

Figure 2C Normality of residuals: The residuals pass Shapiro-Wilk normality test for LMEM of the LN-transformed data. We added very small number (0.0001) to all 0 values in our data set, presented in Fig.2C, D, and Fig.S4 A, to perform natural-log transformation. Details on the LMEM and it’s output are added to the Source data – Statistical analysis file.

Figure 3B Statistic and Scatter: We now show LMEM-derived slope and p-value, indicating deviation of the slope from 0, values in Fig.3 B (below). The LMEM-derived slope has p-value of 0.1925, indicating that the slope is not significantly different from 0. This result changes our original interpretation, and we now edit the associated results and discussion.

Figure 3B Normality of residuals: This data set does not pass Shapiro-Wilk test.

A major issue of the work is also that it is unnecessarily complicated. In the Results section, the authors introduce a number of beta cell subpopulations: first responder cell, last responder cell, wave origin cell, wave end cell, hub-like phase 1, hub-like phase 2, and random cells, which are all defined in exclusively relative terms, regarding the time within which the cells responded, phase lags of their oscillations, or mutual distances within the islet. These cell types also partially overlap.

To address this comment, we added Table 1 to describe the properties of these different populations.

Their choice to use the diameter percentile as a metrics for distances between the cells is not well substantiated since they do not demonstrate in what way would the islet size variability influence the conclusion. All presented islets are of rather a comparable size within the diffusion limits.

We replaced normalized distances in Fig.1 D with absolute distance from first responder in μm.

The functional hierarchy of cells defining the first response should be reflected in the consistency of their relative response time. The authors claim that the spatial organisation is consistent over a time of up to 24 hours. In the first place, it is not clear why would this prolonged consistency be of an advantage in comparison to the absence of such consistency. The linear regression analysis between the initial and repeated relative activation times does suggest a significant correlation, but the distribution of regression residuals of the provided data is again not normal and non-conclusive, despite the low p-value. 50% of the cells defined a first responder in the initial stimulation were part of that subpopulation also during the second stimulation, which is rather random.

We began to describe our analysis of the response time to initial and repeated glucose stimulation earlier in this reply. Further evidence of the distance-dependence of the consistency of the response time is now presented in Fig.S4 A: a response time consistency for cells at 60 μm, 50μm, and 40 μm proximity to the first responder. The closer a cell is located to the first responder, the higher is the consistency of its response time (the lower the scatter), below.

If we analyze this data with a linear regression model, where the r^2 allows us to quantitatively demonstrate decrease of the scatter, we observe r^2 of 0.3013, 0.3228, 0.3674 respectively for cells at 60 μm, 50μm, and 40 μm proximity to the first responder (below). This data is not included in the manuscript because residuals do not pass Shapiro-Wilk Normality test for this model (while they do for the LMEM).

One of the most surprising features of this study is the total lack of fast [Ca2+] oscillations, which are in mouse islets, stimulated with 11 mM glucose typically several seconds long and should be easily detected with the measurement speed used.

Our data used in this manuscript contains Ca2+ dynamics from islets with a) slow oscillations only, b) fast oscillations superimposed on the slow oscillations, c) no obvious oscillations (likely continual spiking). Representative curves are below. Because we focused our study on the slow oscillations, we used dynamics of type (a) in our figures, which formed an impression that no fast oscillations were present. In our analysis of dynamics of type (b) we used Fourier transformation to separate slow oscillations from the fast (described in Methods). Dynamics of type (c) were excluded from the analysis of the oscillatory phase, and instead only used for the first-phase analysis. We indicate this exclusion in the methods.

And lastly, we should also not perpetuate imprecise information about the disease if we know better. The first sentence of the Introduction section, stating that "Diabetes is a disease characterised by high blood glucose, …" is not precise. Diabetes only describes polyuria. Regarding the role of high glucose, a quote from a textbook by K. Frayn, R Evans: Human metabolism - a regulatory perspective, 4rd. 2019 „The changes in glucose metabolism are usually regarded as the "hallmark" of diabetes mellitus, and treatment is always monitored by the level of glucose in the blood. However, it has been said that if it were as easy to measure fatty acids in the blood as it is to measure glucose, we would think of diabetes mellitus mainly as a disorder of fat metabolism."

We acknowledge that Diabetes alone refers to polyurea, and instead state Diabetes Mellitus to be more precise to the disease we refer to. We stated “Diabetes is a disease characterized by high blood glucose, ... “ as this is in line with internationally accepted diagnoses and classification criteria, such as position statements from the American Diabetes Association [‘Diagnosis and Classification of Diabetes Mellitus” AMERICAN DIABETES ASSOCIATION, DIABETES CARE, 36, (2013)]. We certainly acknowledge the glucose-centric approach to characterizing and diagnosing Diabetes Mellitus is largely born of the ease of which glucose can be measured. Thus if blood lipids could be easily measured we may be characterizing diabetes as a disease of hyperlipidemia (depending how lipidemia links with complications of diabetes).

Author Response:

Joint Public Review:

A highly robust result when investigating how neural population activity is impacted by performance in a task is that the trial to trial correlations (noise correlations) between neurons is reduced as performance increases. However the theoretical and experimental literature so far has failed to account for this robust link since reduced noise correlations do not systematically contribute to improved availability or transmission of information (often measured using decoding of stimulus identity). This paper sets out to address this discrepancy by proposing that the key to linking noise correlations to decoding and thus bridging the gap with performance is to rethink the decoders we use : instead of decoders optimized to the specific task imposed on the animal on any given trial (A vs B / B vs C / A vs C), they hypothesize that we should favor a decoder optimized for a general readout of stimulus properties (A vs B vs C).

To test this hypothesis, the authors use a combination of quantitative data analysis and mechanistic network modeling. Data were recorded from neuronal populations in area V4 of two monkeys trained to perform an orientation change detection task, where the magnitude of orientation change could vary across trials, and the change could happen at cued (attended) or uncued (unattended) locations in the visual field. The model, which extends previous work by the authors, reproduces many basic features of the data, and both the model and data offer support for the hypothesis.

The reviewers agreed that this is a potentially important contribution, that addresses a widely observed, but puzzling, relation between perceptual performance and noise correlations. The clarity of the hypothesis, and the combination of data analysis and computational modelling are two essential strengths of the paper.

Overall this paper exhibits a new factor to be taken into account when analysing neural data : the choice of decoder and in particular how general or specific the decoder is. The fact that the generality of the decoder sheds light on the much debated question of noise correlations underscores its importance. The paper therefore opens multiple avenues for future research to probe this new idea, in particular for tasks with multiple stimuli dimensions.

Nonetheless, as detailed below, the reviewers believe the manuscript clarity could be further improved in several points, and some additional analysis of the data would provide more straightforward test of the hypothesis.

1. It would be important to verify that the model reproduces the correlation between noise and signal correlations since this is really a key argument leading to the author's hypothesis.

We have incorporated this verification of the model into the manuscript, as referred to below in the Results:

“Importantly, this model reproduces the correlation between noise and signal correlations (Figure 2–figure supplement 1) observed in electrophysiological data (Cohen & Maunsell, 2009; Cohen & Kohn, 2011). This correlation between the shared noise and the shared tuning is a key component of the general decoder hypothesis. We observed this strong relationship between noise and signal correlations in our recorded neurons (Figure 2–figure supplement 1A) as well as in our modeled data (Figure 2–figure supplement 1B). Using this model, we were able to measure the relationship between noise and signal correlations for varying strengths of attentional modulation. Consistent with the predictions of the general decoder hypothesis, attention weakened the relationship between noise and signal correlations (Figure 2–figure supplement 1C).”

The new figure is as below:

Figure 2–figure supplement 1. The model reproduces the relationship between noise and signal correlations that is key to the general decoder hypothesis. (A) As previously observed in electrophysiological data (Cohen & Maunsell, 2009; Cohen & Kohn, 2011), we observe a strong relationship between noise and signal correlations. During additional recordings collected during most recording sessions (for Monkey 1 illustrated here, n = 37 days with additional recordings), the monkey was rewarded for passively fixating the center of the monitor while Gabors with randomly interleaved orientations were flashed at the receptive field location (‘Stim 2’ location in Figure 1C). The presented orientations spanned the full range of stimulus orientations (12 equally spaced orientations from 0 to 330 degrees). We calculated the signal correlation for each pair of units based on their mean responses to each of the 12 orientations. We define the noise correlation for each pair of units as the average noise correlation for each orientation. The plot depicts signal correlation as a function of noise correlation across all recording sessions, binned into 8 equally sized sets of unit pairs. Error bars represent SEM. (B) The model reproduces the relationship between noise and signal correlations. Signal correlation is plotted as a function of noise correlation, binned into 20 equally sized sets of unit pairs (n = 2000 neurons), for each attentional modulation strength (green: least attended; yellow: most attended). The results were averaged over 50 tested orientations. (C) The slope of the relationship between noise and signal correlations (y-axis) decreases with increasing attentional modulation (x-axis). This suggests that noise is less aligned with signal correlation with increasing attentional modulation.

2. Testing the hypothesis of the general decoder:<br /> 2.1 In the data, the authors compare mainly the specific (stimulus) decoder and the monkey's choice decoder. The general stimulus decoder is only considered in fig. 3f, because data across multiple orientations are available only for the cued condition, and therefore the general and specific decoders cannot be compared for changes between cued and uncued. However, the hypothesized relation between mean correlations and performance should also be true within a fixed attention condition (cued), comparing sessions with larger vs. smaller correlation. In other words, if the hypothesis is correct, you should find that performance of the "most general" decoder (as in fig. 3f) correlates negatively with average noise correlations, across sessions, more so than the "most specific" decoder.<br /> We have added a new supplementary figure to the manuscript:

Figure 3–figure supplement 1. Based on the electrophysiological data, the performance of the monkey’s decoder was more related to mean correlated variability than the performance of the specific decoder within each attention condition. (A) Within the cued attention condition, the performance of the monkey’s decoder was more related to mean correlated variability (left plot; correlation coefficient: n = 71 days, r = -0.23, p = 0.058) than the performance of the specific decoder (right plot; correlation coefficient: r = 0.038, p = 0.75). The correlation coefficients associated with the two decoders were significantly different from each other (Williams’ procedure: t = 3.8, p = 1.5 x 10^-4). Best fit lines plotted in gray. Data from both monkeys combined (Monkey 1 data shown in orange: n = 44 days; Monkey 2 data shown in purple: n = 27 days) with mean correlated variability z-scored within monkey. (B) The data within the uncued attention condition showed a similar pattern, with the performance of the monkey’s decoder more related to mean correlated variability (n = 69 days, r = -0.20, p = 0.14) than the performance of the specific decoder (r = 0.085, p = 0.51; Williams’ procedure: t = 2.0, p = 0.049). Conventions as in (A) (Monkey 1: n = 42 days – see Methods for data exclusions as in Figure 3C; Monkey 2: n = 27 days).

2.2 In figure 3f, a more straightforward and precise comparison is to use the stimulus decoders to predict the choice, and test whether the more specific or the more general can predict choices more accurately.

We have added a new panel to Figure 3 (Figure 3G) that illustrates the results of this analysis comparing whether the specific or more-general decoders predict the monkey’s trial-by-trial choices more accurately:

Figure 3… (G) The more general the decoder (x-axis), the better its performance predicting the monkey’s choices on the median changed orientation trials (y-axis; the proportion of leave-one-out trials in which the decoder correctly predicted the monkey’s decision as to whether the orientation was the starting orientation or the median changed orientation). Conventions as in (F) (see Methods for n values).

The description of this new panel in the Results section is as below:

“Further, the more general the decoder, the better it predicted the monkey’s trial-by-trial choices on the median changed orientation trials (Figure 3G).”

The updated Methods section describing this new panel is as below:

“For Figure 3G, we performanced analyses similar to those performed for Figure 3F, in that we tested each stimulus decoder: ‘1 ori’ decoders (n = 8 decoders; 1 specific decoder for either the first, second, fourth, or fifth largest changed orientation, for each of the 2 monkeys), ‘2 oris’ decoders (n = 12 decoders; 1 decoder for each of the 6 combinations of 2 changed orientations, for each of the 2 monkeys), ‘3 oris’ decoders (n = 8 decoders; 1 decoder for each of the 4 combinations of 3 changed orientations, for each of the 2 monkeys), and ‘4 oris’ decoders (n = 2 decoders; 1 decoder for the 1 combination of 4 changed orientations, for each of the 2 monkeys). However, unlike in Figure 3F, where the performance of the stimulus decoders was compared to the performance of the monkey’s decoder on the median orientation-change trials, here we calculated the performance of the stimulus decoder when tasked with predicting the trial-by-trial choices that the monkey made on the median orientation-change trials. We plotted the proportion of leave-one-out trials in which each decoder correctly predicted the monkey’s choice as to whether the orientation was the starting orientation or the median changed orientation.”

3. The main goal of the manuscript is to determine the impact of noise correlations on various decoding schemes. The figures however only show how decoding co-varies with correlations, but a direct, more causal analysis of the effect of correlations on decoding seems to be missing. Such an analysis can be obtained by comparing decoding on simultaneously recorded activity with decoding on trial-shuffled activity, in which noise-correlations are removed.

We have added the following Discussion section to address this point:

“The purpose of this study was to investigate the relationship between mean correlated variability and a general decoder. We made an initial test of the overarching hypothesis that observers use a general decoding strategy in feature-rich environments by testing whether a decoder optimized for a broader range of stimulus values better matched the decoder actually used by the monkeys than a specific decoder optimized for a narrower range of stimulus values. We purposefully did not make claims about the utility of correlated variability relative to hypothetical situations in which correlated variability does not exist in the responses of a group of neurons, as we suspect that this is not a physiologically realistic condition. Studies that causally manipulate the level of correlated variability in neuronal populations to measure the true physiological and behavioral effects of increasing or decreasing correlated variability levels, through pharmacological or genetic means, may provide important insights into the impact of correlated variability on various decoding strategies.”

4. How different are the four different decoders (specific/monkey, cued/uncued)? It would be interesting to see how much they overlap. More generally, the authors should discuss the alternative that attention modulates also the readout/decoding weights, rather than or in addition to modulating V4 activity.

We have added the following to the manuscript:

“A fixed readout mechanism

A prior study from our lab found that attention, rather than changing the neuronal weights of the observer’s decoder, reshaped neuronal population activity to better align with a fixed readout mechanism (Ruff & Cohen, 2019). To test whether the neuronal weights of the monkey’s decoder changed across attention conditions (attended versus unattended), Ruff and Cohen switched the neuronal weights across conditions, testing the stimulus information in one attention condition with the neuronal weights from the other. They found that even with the switched weights, the performance of the monkey’s decoder was still higher in the attended condition. The results of this study support the conclusion that attention reshapes neuronal activity so that a fixed readout mechanism can better read out stimulus information. In other words, differences in the performance of the monkey’s decoder across attention conditions may be due to differences in how well the neuronal activity aligns with a fixed decoder.

Our study extends the findings of Ruff and Cohen to test whether that fixed readout mechanism is determined by a general decoding strategy. Our findings support the hypothesis that observers use a general decoding strategy in the face of changing stimulus and task conditions. Our findings do not exclude other potential explanations for the suboptimality of the monkey’s decoder, nor do they exclude the possibility that attention modulates decoder neuronal weights. However, our findings together with those of Ruff and Cohen shed light on why neuronal decoders are suboptimal in a manner that aligns the fixed decoder axis with the correlated variability axis (Ni et al., 2018; Ruff et al., 2018).”

5. Quantifying the link between model and data :<br /> 5.1 the text providing motivation for the model could be improved. The motivation used in the manuscript is, essentially, that the model allows to extrapolate beyond the data (more stimuli, more repetitions, more neurons). The dangers of extrapolation beyond the range of the data are however well known. A model that extrapolates beyond existing data is useful to design new experiments and test predictions, but this is not done here. Because the manuscript is about information and decoding, a better motivation is the fact that this model takes an actual image as input, and produces tuning and covariance compatible with each other because they are constrained by an actual network that processes the input (as opposed to parametric models where tuning and covariance can be manipulated independently).

We have modified the manuscript as below:

“Here, we describe a circuit model that we designed to allow us to compare the specific and monkey’s decoders from our electrophysiological dataset to modeled ideal specific and general decoders. The primary benefit of our model is that it can take actual images as inputs and produce neuronal tuning and covariance that are compatible with each other because of constraints from the simulated network that processed the inputs (Huang et al., 2019). Parametric models in which tuning and covariance can be manipulated independently would not provide such constraints. In our model, the mean correlated variability of the population activity is restricted to very few dimensions, matching experimentally recorded data from visual cortex demonstrating that mean correlated variability occupies a low-dimensional subset of the full neuronal population space (Ecker et al., 2014; Goris et al., 2014; Huang et al., 2019; Kanashiro et al., 2017; Lin et al., 2015; Rabinowitz et al., 2015; Semedo et al., 2019; Williamson et al., 2016).”

“Our study also demonstrates the utility of combining electrophysiological and circuit modeling approaches to studying neural coding. Our model mimicked the correlated variability and effects of attention in our physiological data. Critically, our model produced neuronal tuning and covariance based on the constraints of an actual network capable of processing images as inputs.”

We have also removed the Results and Discussion text that suggested that the model allowed us to extrapolate beyond the data.

5.2 The ring structure, and the orientation of correlations (Fig 2b) seem to be key ingredients of the model, but are they based on data, or ad-hoc assumptions?

We have modified the manuscript to clarify this point, as below:

“As the basis for our modeled general decoder, we first mapped the n-dimensional neuronal activity of our model in response to the full range of orientations to a 2-dimensional space. Because the neurons were tuned for orientation, we could map the n-dimensional population responses to a ring (Figure 2B, C). The orientation of correlations (the shape of each color cloud in Figure 2B) was not an assumed parameter, and illustrates the outcome of the correlation structure and dimensionality modeled by our data. In Figure 2B, we can see that the fluctuations along the radial directions are much larger than those along other directions for a given orientation. This is consistent with the low-dimensional structure of the modeled neuronal activity. In our model, the fluctuations of the neurons, mapped to the radial direction on the ring, were more elongated in the unattended state (Figure 2B) than in the attended state (Figure 2C).”

5.3 In the model, the specific decoder is quite strongly linked to correlated variability and the improvement of the general decoder is clear but incremental (0.66 vs 0.83) whereas in the data there really is no correlation at all (Fig 3c). This is a bit problematic because the author's begin by stating that specific decoders cannot explain the link between noise correlations and accuracy but their specific decoder clearly shows a link.

We appreciate this point and have modified the manuscript as below:

“Indeed, we found that just as the performance of the physiological monkey’s decoder was more strongly related to mean correlated variability than the performance of the physiological specific decoder (Figure 3C; see Figure 3–figure supplement 1 for analyses per attention condition), the performance of the modeled general decoder was more strongly related to mean correlated variability than the performance of the modeled specific decoder (Figure 3D). We modeled much stronger relationships to correlated variability (Figure 3D) than observed with our physiological data (Figure 3C). We observed that the correlation with specific decoder performance was significant with the modeled data but not with the physiological data. This is not surprising as we saw attentional effects, albeit small ones, on specific decoder performance with both the physiological and the modeled data (Figure 3A, B). Even small attentional effects would result in a correlation between decoder performance and mean correlated variability with a large enough range of mean correlated variability values. It is possible that with enough electrophysiological data, the performance of the specific decoder would be significantly related to correlated variability, as well. As described above, our focus is not on whether the performance of any one decoder is significantly correlated with mean correlated variability, but on which decoder provides a better explanation of the frequently observed relationship between performance and mean correlated variability. The performance of the general decoder was more strongly related to mean correlated variability than the performance of the specific decoder.”

“Our results suggest that the relationship between behavior and mean correlated variability is more consistent with observers using a more general strategy that employs the same neuronal weights for decoding any stimulus change.”

6. General decoder: Some parts of the text (eg. Line 60, Line 413) refer to a decoder that accounts for discrimination along different stimulus dimensions (eg. different values of orientation, or different color of the visual input). But the results of the manuscripts are about a general decoder for multiple values along a single stimulus dimension. The disconnect should be discussed, and the relation between these two scenarios explained.

We have modified the manuscript as below:

“Here, we report the results of an initial test of this overarching hypothesis, based on a single stimulus dimension. We used a simple, well-studied behavioral task to test whether a more-general decoder (optimized for a broader range of stimulus values along a single dimension) better explained the relationship between behavior and mean correlated variability than a more-specific decoder (optimized for a narrower range of stimulus values along a single dimension). Specifically, we used a well-studied orientation change-detection task (Cohen & Maunsell, 2009) to test whether a general decoder for the full range of stimulus orientations better explained the relationship between behavior and mean correlated variability than a specific decoder for the orientation change presented in the behavioral trial at hand.

This test based on a single stimulus dimension is an important initial test of the general decoder hypothesis because many of the studies that found that performance increased when mean correlated variability decreased used a change-detection task…”

“We performed this initial test of the overarching general decoder hypothesis in the context of a change-detection task along a single stimulus dimension because this type of task was used in many of the studies that reported a relationship between perceptual performance and mean correlated variability (Cohen & Maunsell, 2009; 2011; Herrero et al., 2013; Luo & Maunsell, 2015; Mayo & Maunsell, 2016; Nandy et al., 2017; Ni et al., 2018; Ruff & Cohen, 2016; 2019; Verhoef & Maunsell, 2017; Yan et al., 2014; Zénon & Krauzlis, 2012). This simple and well-studied task provided an ideal initial test of our general decoder hypothesis.

This initial test of the general decoder hypothesis suggests that a more general decoding strategy may explain observations in studies that use a variety of behavioral and stimulus conditions.”

“This initial study of the general decoder hypothesis tested this idea in the context of a visual environment in which stimulus values only changed along a single dimension. However, our overarching hypothesis is that observers use a general decoding strategy in the complex and feature-rich visual scenes encountered in natural environments. In everyday environments, visual stimuli can change rapidly and unpredictably along many stimulus dimensions. The hypothesis that such a truly general decoder explains the relationship between perceptual performance and mean correlated variability is suggested by our finding that the modeled general decoder for orientation was more strongly related to mean correlated variability than the modeled specific decoder (Figure 3D). Future tests of a general decoder for multiple stimulus features would be needed to determine if this decoding strategy is used in the face of multiple changing stimulus features. Further, such tests would need to consider alternative hypotheses for how sensory information is decoded when observing multiple aspects of a stimulus (Berkes et al., 2009; Deneve, 2012; Lorteije et al., 2015). Studies that use complex or naturalistic visual stimuli may be ideal for further investigations of this hypothesis.”

7. Some statements in the discussion such as l 354 "the relationship between behavior and mean correlated variability is explained by the hypothesis that observers use a general strategy" should be qualified : the authors clearly show that the general decoder amplifies the relationship but in their own data the relationship exists already with a specific decoder.

We have modified the manuscript as below:

“Our results suggest that the relationship between behavior and mean correlated variability is more consistent with observers using a more general strategy that employs the same neuronal weights for decoding any stimulus change.

“Together, these results support the hypothesis that observers use a more general decoding strategy in scenarios that require flexibility to changing stimulus conditions.”

“This initial test of the general decoder hypothesis suggests that a more general decoding strategy may explain observations in studies that use a variety of behavioral and stimulus conditions.”

8. Low-Dimensionality, beginning of Introduction and end of Discussion: experimentally, cortical activity is low-dimensional, and the proposed model captures that. But some of the reviewers did not understand the argument offered for why this matters, for the relation between average correlations and performance. It seems that the dimensionality of the population covariance is not relevant: The point instead is that a change in amplitude of fluctuations along the f'f' direction necessarily impact performance of a "specific" decoder, whereas changes in all other dimensions can be accounted for by the appropriate weights of the "specific" decoder. On the other hand, changes in fluctuation strength along multiple directions may impact the performance of the "general" decoder.

We have modified the manuscript as below:

“These observations comprise a paradox because changes in this simple measure should have a minimal effect on information coding. Recent theoretical work shows that neuronal population decoders that extract the maximum amount of sensory information for the specific task at hand can easily ignore mean correlated noise (Kafashan et al., 2021; Kanitscheider et al., 2015b; Moreno-Bote et al., 2014; Pitkow et al., 2015; Rumyantsev et al., 2020; for review, see Kohn et al., 2016). Decoders for the specific task at hand can ignore mean correlated variability because it does not corrupt the dimensions of neuronal population space that are most informative about the stimulus (Moreno-Bote et al., 2014).”

“Our results address a paradox in the literature. Electrophysiological and theoretical evidence supports that there is a relationship between mean correlated variability and perceptual performance (Abbott & Dayan, 1999; Clery et al., 2017; Haefner et al., 2013; Jin et al., 2019; Ni et al., 2018; Ruff & Cohen, 2019; reviewed by Ruff et al., 2018). Yet, a specific decoding strategy in which different sets of neuronal weights are used to decode different stimulus changes cannot easily explain this relationship (Kafashan et al., 2021; Kanitscheider et al., 2015b; Moreno-Bote et al., 2014; Pitkow et al., 2015; Rumyantsev et al., 2020; reviewed by Kohn et al., 2016). This is because specific decoders of neuronal population activity can easily ignore changes in mean correlated noise (Moreno-Bote et al., 2014).”

Author Response:

Reviewer #1 (Public Review):

The introduction felt a bit short. I was hoping early on I think for a hint at what biotic and abiotic factors UV could be important for and how this might be important for adaptation. A bit more on previous work on the genetics of UV pigmentation could be added too. I think a bit more on sunflowers more generally (what petiolaris is, where natural pops are distributed, etc.) would be helpful. This seems more relevant than its status as an emoji, for example.

We had opted to provide some of the relevant background in the corresponding sections of the manuscript, but agree that it would be beneficial to expand the introduction. In the revised version of the manuscript, we have modified the introduction and the first section of Results and Discussion to include more information about wild sunflowers, possible adaptive functions of floral UV patterns, and previous work on the genetic basis of floral UV patterning. More generally, we have strived to provide more background information throughout the manuscript.

The authors present the % of Vp explained by the Chr15 SNP. Perhaps I missed it, but it might be nice to also present the narrow sense heritability and how much of Va is explained.

Narrow sense heritability for LUVp is extremely high in our H. annuus GWAS population; four different software [EMMAX (Kang et al., Nat Genet 2010), GEMMA (Zhou and Stephens, Nat Genet. 2012), GCTA (Yang et al., Am J Hum Genet 2011) and BOLT_LMM (Loh et al., Nat Genet 2015)] provided h2 estimates of ~1. While it is possible that these estimates are somewhat inflated by the presence of a single locus of extremely large effect, all individuals in this populations were grown at the same time under the same conditions, and limited environmental effects would therefore be expected. The percentage of additive variance explained by HaMYB111 appears therefore to be equal to the percentage of phenotypic variance (~62%).

We have included details in the Methods section – Genome-wide association mapping, and added this information to the relevant section of the main text:

“The chromosome 15 SNP with the strongest association with ligule UV pigmentation patterns in H. annuus (henceforth “Chr15_LUVp SNP”) explained 62% of the observed phenotypic and additive variation (narrow-sense heritability for LUVp in this dataset is ~1).”

A few lines of discussion about why the Chr15 allele might be observed at only low frequencies in petiolaris I think would be of interest - the authors appear to argue that the same abiotic factors may be at play in petiolaris, so why don't we see this allele at frequencies higher than 2%? Is it recent? Geographically localized?

That is a very interesting observation, and we currently do not have enough data to provide a definitive answer to why that is. From GWAS, HaMYB111 does not seem to play a measurable role in controlling variation for LUVp in H. petiolaris; Even when we repeat the GWAS with MAF > 1%, so that the Chr15_LUVp SNP would be included in the analysis, there is no significant association between that SNP and LUVp (the significant association on chr. 15 seen in the Manhattan plot for H. petiolaris is ~20 Mbp downstream of HaMYB111). The rarity of the L allele in H. petiolaris could complicate detection of a GWAS signal; on the other hand, the few H. petiolaris individuals carrying the L allele have, on average, only marginally larger LUVp than the rest of the population (LL = 0.32 allele).

The two most likely explanations for the low frequencies of the L allele in H. petiolaris are differences in alleles, or their effect, between H. annuus and H. petiolaris; or, as suggested by the reviewer, a recent introgression. In H. annuus, the Chr15_LUVp SNP is likely not the actual causal polymorphism affecting HaMYB111 activity, but is only in LD with it (or them); this association might be absent in H. petiolaris alleles. An alternative possibility is that downstream differences in the genetic network regulating flavonol glycosides biosynthesis mask the effect of different HaMYB111 alleles.

H. annuus and H. petiolaris hybridize frequently across their range, so this could be a recent introgression that has not established itself; alternatively, physiological differences in H. petiolaris could make the L allele less advantageous, so the introgressed allele is simply being maintained by drift (or recurring hybridization). Further analysis of genetic and functional diversity at HaMYB111 in H. petiolaris will be required to differentiate between these possibilities.

We have added a few sentences highlighting some of these possible explanations at the end the main text of the manuscript, which now reads:

“Despite a more limited range of variation for LUVp, a similar trend (larger UV patterns in drier, colder environments) is present also in H. petiolaris (Figure 4 – figure supplement 4). Interestingly, while the L allele at Chr_15 LUVp SNP is present in H. petiolaris (Figure 1 – figure supplement 2), it is found only at a very low frequency, and does not seem to significantly affect floral UV patterns in this species (Figure 2a). This could represent a recent introgression, since H. annuus and H. petiolaris are known to hybridize in nature (Heiser, 1947, Yatabe et al., 2007). Alternatively, the Chr_15 LUVp SNP might not be associated with functional differences in HaMYB111 in H. petiolaris, or differences in genetic networks or physiology between H. annuus and H. petiolaris could mask the effect of this allele, or limit its adaptive advantage, in the latter species.“

Page 14: It's unclear to me why there is any need to discretize the LUVp values for the analyses presented here. Seems like it makes sense to either 1) analyze by genotype of plant at the Chr15 SNP, if known, or 2) treat it as a continuous variable and analyze accordingly.

We designed our experiment to be a comparison between three well-defined phenotypic classes, to reduce the experimental noise inherent to pollinator visitation trials. As a consequence, intermediate phenotypic classes (0.3 < LUVp < 0.5 and 0.8 < LUVp < 0.95) are not represented in the experiment, and therefore we believe that analyzing LUVp as a continuous variable would be less appropriate in this case. In the revised manuscript, we have provided a modified Figure 4 – figure supplement 1 in which individual data points are show (colour-coded by pollinator type), as well as a fitted lines showing the general trend across the data.

The individuals in pollinator visitation experiments were not genotyped for the Chr15_LUVp SNP; while having that information might provide a more direct link between HaMYB111 and pollinator visitation rates, our main interest in this experiment was to test the possible adaptive effects of variation in floral UV pigmentation.

Page 14: I'm not sure you can infer selection from the % of plants grown in the experiment unless the experiment was a true random sample from a larger metapopulation that is homogenous for pollinator preference. In addition, I thought one of the Ashman papers had actually argued for intermediate level UV abundance in the presence of UV?

We have removed mentions of selection from the sentence - while the 110 populations included in our 2019 common garden experiment were selected to represent the whole range of H. annuus, we agree that the pattern we observe is at best suggestive. We have, however, kept a modified version of the sentence in the revised version of the manuscript, since we believe that is an interesting observation. The sentence now reads:

“Pollination rates are known to be yield-limiting in sunflower (Greenleaf and Kremen, 2006), and a strong reduction in pollination could therefore have a negative effect on fitness; consistent with this plants with very small LUVp values were rare (~1.5% of individuals) in our common garden experiment, which was designed to provide a balanced representation of the natural range of H. annuus.”. (new lines 373-378)

It is correct that Koski et al., Nature Plants 2015 found intermediate UV patterns to increase pollen viability in excised flowers of Argentina anserina exposed to artificial UV radiation. However, the authors also remark that larger UV patterns would probably be favoured in natural environments, in which UV radiation would be more than two times higher than in their experimental setting. Additionally, when using artificial flowers, they found that pollen viability increased linearly with the size of floral UV pattern.

More generally, as we discuss later on in the manuscript, the pollen protection mechanism proposed in Koski et al., Nature Plants 2015 is unlikely to be as important in sunflower inflorescences, which are much flatter than the bowl- shaped flowers of A. anserina; consistent with this, and contrary to what was observed for A. anserina, we found no correlation between UV radiation and floral UV patterns in wild sunflowers (Figure 4c).

I would reduce or remove the text around L316-321. If there's good a priori reason to believe flower heat isn't a big deal (L. 323) and the experimental data back that up, why add 5 lines talking up the hypothesis?

We had fairly strong reasons to believe temperature might play an important role in floral UV pattern diversity: a link between flower temperature and UV patterns has been proposed before (Koski et al., Current Biol 2020); a very strong correlation exists between temperature and LUVp in our dataset; and, perhaps more importantly, inflorescence temperature is known to have a major effect on pollinator attraction (Atamian et al., Science 2016; Creux et al., New Phytol 2021). While it is known that UV radiation is not particularly energetic, we didn’t mean line 323 to imply that we were sure a priori that there wouldn’t be any effect of UV patterns of inflorescence temperature.

In the revised manuscript, we have re-organized that section and provided the information reported in line 323 (UV radiation accounts for only 3-7% of the total radiation at earth level) before the experimental results, to clarify what our thought process was in designing those experiments. The paragraph now reads:

“By absorbing more radiation, larger UV bullseyes could therefore contribute to increasing temperature of the sunflower inflorescences, and their attractiveness to pollinators, in cold climates. However, UV wavelengths represents only a small fraction (3-7%) of the solar radiation reaching the Earth surface (compared to >50% for visible wavelengths), and might therefore not provide sufficient energy to significantly warm up the ligules (Nunez et al., 1994). In line with this observation, different levels of UV pigmentation had no effect on the temperature of inflorescences or individual ligules exposed to sunlight (Figure 4e-g; Figure 4 – figure supplement 3).”

Page 17: The discussion of flower size is interesting. Is there any phenotypic or genetic correlation between LUVP and flower size?

This is a really interesting question! There is no obvious genetic correlation between LUVp and flower size – in GWAS, HaMYB111 is not associated to any of the floral characteristics we measured (flowerhead diameter; disk diameter; ligule length; ligule width; relative ligule size; see Todesco et al., Nature 2020). There is also no significant association between ligule length and LUVp (R^2 = 0.0024, P = 0.1282), and only a very weak positive association between inflorescence size and LUVp (R^2 = 0.0243, P = 0.00013; see attached figure). There is, however, a stronger positive correlation between LUVp and disk size (the disk being the central part of the sunflower inflorescence, composed of the fertile florets; R^2 = 0.1478. P = 2.78 × 10-21), and as a consequence a negative correlation between LUVp and relative ligule size (that is, the length of the ligule relative to the diameter of the whole inflorescence; R^2 = 0.1216, P = 1.46 × 10-17). This means that, given an inflorescence of the same size, plants with large LUVp values will tend to have smaller ligules and larger discs. Since the disk of sunflower inflorescences is uniformly UV- absorbing, this would further increase the size of UV-absorbing region in these inflorescences.

While it is tempting to speculate that this might be connected with regulation of transpiration (meaning that plants with larger LUVp further reduce transpiration from ligules by having smaller ligules - relative ligule size is also positively correlated with summer humidity; R^2 = 0.2536, P = 2.86 × 10_-5), there are many other fitness-related factors that could determine inflorescence size, and disk size in particular (seed size, florets/seed number...). Additionally, in common garden experiments, flowerhead size (and plant size in general) is affected by flowering time, which is also one of the reason why we use LUVp to measure floral UV patterns instead of absolute measurements of bullseye size; in a previous work from our group in Helianthus argophyllus, size measurements for inflorescence and UV bullseye mapped to the same locus as flowering time, while genetic regulation of LUVp was independent of flowering time (Moyers et al., Ann Bot 2017). Flowering time in H. annuus is known to be strongly affected by photoperiod (Blackman et al., Mol Ecol 2011), meaning that the flowering time we measured in Vancouver might not reflect the exact flowering time in the populations of origin of those plants – with consequences on inflorescence size.

In summary, there is an interesting pattern of concordance between floral UV pattern and some aspects of inflorescence morphology, but we think it would be premature to draw any inference from them. Measurements of inflorescence parameters in natural populations would be much more informative in this respect.

Reviewer #2 (Public Review):

The genetic analysis is rigorously conducted with multiple Helianthus species and accessions of H. annuus. The same QTL was inputed in two Helianthus species, and fine mapped to promotor regions of HaMyb111.

While there is a significant association at the beginning of chr. 15 in the GWAS for H. petiolaris petiolaris, we should clarify that that peak is unfortunately ~20 Mbp away from HaMYB111. While it is not impossible that the difference is due to reference biases in mapping H. petiolaris reads to the cultivated H. annuus genome, the most conservative explanation is that those two QTL are unrelated. We have clarified this in the legend to Fig. 2 in the revised manuscript.

The allelic variation of the TF was carefully mapped in many populations and accessions. Flavonol glycosides were found to correlate spatially and developmentally in ligules and correlate with Myb111 transcript abundances, and a downstream flavonoid biosynthetic gene. Heterologous expression in Arabidopsis in Atmyb12 mutants, showed that HaMyb111 to be able to regulate flavonol glycoside accumulations, albeit with different molecules than those that accumulate in Helianthus. Several lines of evidence are consistent with transcriptional regulation of myb111 accounting for the variation in bullseye size.

Functional analysis examined three possible functional roles, in pollinator attraction, thermal regulation of flowers, and water loss in excised flowers (ligules?), providing support for the first and last, but not the second possible functions, confirming the results of previous studies on the pollinator attraction and water loss functions for flavonol glycosides. The thermal imaging work of dawn exposed flower heads provided an elegant falsification of the temperature regulation hypothesis. Biogeographic clines in bullseye size correlated with temperature and humidity clines, providing a confirmation of the hypothesis posed by Koski and Ashmann about the patterns being consistent with Gloger's rule, and historical trends from herbaria collections over climate change and ozone depletion scenarios. The work hence represents a major advance from Moyers et al. 2017's genetic analysis of bullseyes in sunflowers, and confirms the role established in Petunia for this Myb TF for flavonoid glycoside accumulations, in a new tissue, the ligule.

Thank you. We have specified in the legend of Fig. 4i of the revised manuscript that desiccation was measured in individual detached ligules, and added further details about the experiment in the Methods section.

While there is a correlation between pigmentation and temperature/humidity in our dataset, it goes in the opposite direction to what would be expected under Gloger’s rule – that is, we see stronger pigmentation in drier/colder environments, contrary to what is generally observed in animals. This is also contrary to what observed in Koski and Ashman, Nature Plants 2015, where the authors found that floral UV pigmentation increased at lower latitudes and higher levels of UV radiation. While possibly rarer, such “anti-Gloger” patterns have been observed in plants before (Lev-Yadun, Plant Signal Behav 2016).

Weakness: The authors were not able to confirm their inferences about myb111 function through direct manipulations of the locus in sunflower.

That is unfortunately correct. Reliable and efficient transformation of cultivated sunflower (much less of wild sunflower species) has eluded the sunflower community (including our laboratories) so far – see for example discussion on the topic in Lewi et al. Agrobacterium protocols 2016, and Sujatha et al. PCTOC 2012. We had therefore to rely on heterologous complementation in Arabidopsis; while this approach has limitations, we believe that its results, given also the similarity in expression patterns between HaMYB111 and AtMYB111, and in combination with the other experiments reported in our manuscript, make a convincing case that HaMYB111 regulates flavonol glycosides accumulation in sunflower ligules.

Given that that the flavonol glycosides that accumulate in Helianthus are different from those regulated when the gene is heterologously expressed in Arabidopsis, the biochemical function of Hamyb111, while quite reasonable, is not completely watertight. The flavonol glycosides are not fully characterized (only Ms/Ms data are provided) and named only with cryptic abbreviations in the main figures.

We believe that the fact that expression of HaMYB111 in the Arabidopsis myb111 mutant reproduces the very same pattern of flavonol glycosides accumulation found in wild type Col-0 is proof that its biochemical function is the same as that of the endogenous AtMYB111 gene – that is, HaMYB111 induces expression of the same genes involved in flavonol glycosides biosynthesis in Arabidopsis. Differences in function between HaMYB11 and AtMYB111 would have resulted in different flavonol profiles between wild type Col-0 and 35S::HaMYB111 myb111 lines. It should be noted that the known direct targets of AtMYB111 in Arabidopsis are genes involved in the production of the basic flavonol aglycone (Strake et al., Plant J 2007). Differences in flavonol glycoside profiles between the two species are likely due to broader differences between the genetic networks regulating flavonol biosynthesis: additional layers of regulation of the genes targeted by MYB111, or differential regulation (or presence/absence variation) of genes controlling downstream flavonol glycosylation and conversion between different flavonols.

In the revised manuscript, we have added the full names of all identified peaks to the legend of Figures 3a,b,e.

This and the differences in metabolite accumulations between Arabidopsis and Helianthus becomes a bit problematic for the functional interpretations. And here the authors may want to re-read Gronquist et al. 2002: PNAS as a cautionary tale about inferring function from the spatial location of metabolites. In this study, the Eisner/Meinwald team discovered that imbedded in the UV-absorbing floral nectar guides amongst the expected array of flavonoid glycosides, were isoprenilated phloroglucinols, which have both UV-absorbing and herbivore defensive properties. Hence the authors may want to re-examine some of the other unidentified metabolites in the tissues of the bullseyes, including the caffeoyl quinic acids, for alternative functional hypotheses for their observed variation in bullseye size (eg. herbivore defense of ligules).

This is a good point, and we have included a mention of a more explicit mention possible role of caffeoyl quinic acid (CQA) as a UV pigment in the main text, as well as highlighted at the end of the manuscript other possible factors that could contribute to variation for floral UV patterns in wild sunflowers.

We should note, however, that CQA plays a considerably smaller role than flavonols in explaining UV absorbance in UV-absorbing (parts of) sunflower ligules, and the difference in abundance with respect to UV-reflecting (parts of) ligules is much less obvious than for flavonols (height of the absorbance peak is reduced only 2-3 times in UV- reflecting tissues for CQA, vs. 7-70 fold reductions for individual quercetin glycosides). Therefore, flavonols are clearly the main pigment responsible for UV patterning in ligules. This is in contrast with the situation for Hypericum calycinum reported in Gronquist et al., PNAS 2002, were dearomatized isoprenylated phloroglucinols (DIPs) are much more abundant than flavonols in most floral tissue, including petals. The localization of DIPs accumulation, in reproductive organs and on the abaxial (“lower”) side of the petals (so that they would be exposed when the flower is closed), is also more consistent with a role in prevention of herbivory; no UV pigmentation is found on the adaxial (“upper”) part of petals in this species, which would be consistent with a role in pollinator attraction.

The hypotheses regarding a role for the flavonoid glycosides regulated by Myb111 expression in transpirational mitigation and hence conferring a selective advantage under high temperatures and low and high humidities, are not strongly supported by the data provided. The water loss data from excised flowers (or ligules-can't tell from the methods descriptions) is not equivalent to measures of transpiration rates (the stomatal controlled release of water), which are better performed with intact flowers by porometry or other forms of gas-exchange measures. Excised tissues tend to have uncontrolled stomatal function, and elevated cuticular water loss at damaged sites. The putative fitness benefits of variable bullseye size under different humidity regimes, proposed to explain the observed geographical clines in bullseye size remain untested.

We have clarified in the text and methods section that the desiccation experiments were performed on detached ligules. We agree that the results of this experiments do not constitute a direct proof that UV patterns/flavonol levels have an impact on plant fitness under different humidities in the wild – our aim was simply to provide a plausible physiological explanation for the correlation we observe between floral UV patterns and relative humidity. However, we do believe they are strongly suggestive of a role for floral flavonol/UV patterns in regulating transpiration, which is consistent with previous observations that flowers are a major source of transpiration in plants (Galen et al., Am Nat 2000, and other references in the manuscript). As suggested also by other reviewers, we have softened our interpretation of these result to clarify that they are suggestive, but not proof, of a connection between floral UV patterns, ligule transpiration and environmental humidity levels.

“While desiccation rates are only a proxy for transpiration in field conditions (Duursma et al. 2019, Hygen et al. 1951), and other factors might affect ligule transpiration in this set of lines, this evidence (strong correlation between LUVp and summer relative humidity; known role of flavonol glycosides in regulating transpiration; and correlation between extent of ligule UV pigmentation and desiccation rates) suggests that variation in floral UV pigmentation in sunflowers is driven by the role of flavonol glycosides in reducing water loss from ligules, with larger floral UV patterns helping prevent drought stress in drier environments.” (new lines 462-469)

Detached ligules were chosen to avoid confounding the results should differences in the physiology of the rest of the inflorescence/plant between lines also affect rates of water loss. Desiccation/water loss measurements were performed for consistency with the experiments reported in Nakabayashi et al Plant J. 2014, in which the effects of flavonol accumulation (through overexpression of AtMYB12) on water loss/drought resistance were first reported. It should also be noted that the use of detached organs to study the effect of desiccation on transpiration, water loss and drought responses is common in literature (see for example Hygen, Physiol Plant 1951; Aguilar et al., J Exp Bot 2000; Chen et al., PNAS 2011; Egea et al., Sci Rep 2018; Duursma et al., New Phytol 2019, among others). While removing the ligules create a more stressful/artificial situation, mechanical factors are likely to affect all ligules and leaves in the same way, and we can see no obvious reason why that would affect the small LUVp group more than the large LUVp group (individuals in the two groups were selected to represent several geographically unrelated populations).

We have included some of the aforementioned references to the main text and Methods sections in the revised manuscript to support our use of this experimental setup.

Alternative functional hypotheses for the observed variation in bullseye size in herbivore resistance or floral volatile release could also be mentioned in the Discussion. Are the large ligules involved in floral scent release?

We have added sentences in the Results and Discussion, and Conclusions section in the revised manuscript to explore possible additional factors that could influence patterns of UV pigmentation across sunflower populations, including resistance to herbivory and floral volatiles. While some work has been done to characterize floral volatiles in sunflower (e.g. Etievant et al. J. Agric. Food Chem; Pham-Delegue et al. J. Chem. Ecol. 1989), to our knowledge the role of ligules in their production has not been investigates.

In the revised manuscript, the section “A dual role for floral UV pigmentation” now includes the sentences:

“Although pollinator preferences in this experiment could still affected by other unmeasured factors (nectar content, floral volatiles), these results are consistent with previous results showing that floral UV patterns play a major role in pollinator attraction (Horth et al., 2014, Koski ad Ashman, 2014, Rae and Vamosi, 2013, Sheehan et al., 2016).” (new lines 378-381)

And the Conclusions sections includes the sentence:

“It should be noted that, while we have examined some of the most likely factors explaining the distribution of variation for floral UV patterns in wild H. annuus across North America, other abiotic factors could play a role, as well as biotic ones (e.g. the aforementioned differences in pollinator assemblages, or a role of UV pigments in protection from herbivory (Gronquist et al., 2001)).” (new lines 540-544)

Reviewer #3 (Public Review):

Todesco et al undertake an ambitious study to understand UV-absorbing variation in sunflower inflorescences, which often, but not always display a "bullseye" pattern of UV-absorbance generated by ligules of the ray flowers. [...] I think this manuscript has high potential impact on science on both of these fronts.

Thank you! We are aware that our experiments do not provide a direct link between UV patterns and fitness in natural populations (although we think they are strongly suggestive) and that, as pointed out also by other reviewers, there are other possible (unmeasured) factors that could explain or contribute to explain the patterns we observed. In the revised manuscript we have better characterized the aims and interpretation of our desiccation experiment, and modified the main text to acknowledge other possible factors affecting pollination preferences (nectar production, floral volatiles) and variation for floral UV patterns in H. annuus (pollinator assemblages, resistance to herbivory).

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:

1) The user manual and tutorial are well documented, although the actual code could do with more explicit documentation and comments throughout. The overall organisation of the code is also a bit messy.

We have now implemented an ongoing, automated code review via Codacy (https://app.codacy.com/gh/caseypaquola/BigBrainWarp/dashboard). The grade is published as a badge on GitHub. We improved the quality of the code to an A grade by increasing comments and fixing code style issues. Additionally, we standardised the nomenclature throughout the toolbox to improve consistency across scripts and we restructured the bigbrainwarp function.

2) My understanding is that this toolbox can take maps from BigBrain to MRI space and vice versa, but the maps that go in the direction BigBrain->MRI seem to be confined to those provided in the toolbox (essentially the density profiles). What if someone wants to do some different analysis on the BigBrain data (e.g. looking at cellular morphology) and wants that mapped onto MRI spaces? Does this tool allow for analyses that involve the raw BigBrain data? If so, then at what resolution and with what scripts? I think this tool will have much more impact if that was possible. Currently, it looks as though the 3 tutorial examples are basically the only thing that can be done (although I may be lacking imagination here).

The bigbrainwarp function allows input of raw BigBrain data in volume and surface forms. For volumetric inputs, the image must be aligned to the full BigBrain or BigBrainSym volume, but the function is agnostic to the input voxel resolution. We have also added an option for the user to specify the output voxel resolution. For example,

bigbrainwarp --in_space bigbrain --in_vol cellular_morphology_in_bigbrain.nii \ --interp linear --out_space icbm --out_res 0.5 \ --desc cellular_morphology --wd working_directory

where “cellular_morphology_in_bigbrain.nii” was generated from a BigBrain volume (see Table 2 below for all parameters). The BigBrain volume may be the 100-1000um resolution images provided on the ftp or a resampled version of these images, as long as the full field of view is maintained. For surface-based inputs, the data must contain a value for each vertex of the BigBrain/BigBrainSym mesh. We have clarified these points in the Methods, illustrated the potential transformations in an extended Figure 3 and highlighted the distinctiveness of the tutorial transformations in the Results.

3) An obvious caveat to bigbrain is that it is a single brain and we know there are sometimes substantial individual variations in e.g. areal definition. This is only slightly touched upon in the discussion. Might be worth commenting on this more. As I see it, there are multiple considerations. For example (i) Surface-to-Surface registration in the presence of morphological idiosyncracies: what parts of the brain can we "trust" and what parts are uncertain? (ii) MRI parcellations mapped onto BigBrain will vary in how accurately they may reflect the BigBrain areal boundaries: if histo boundaries do not correspond with MRI-derived ones, is that because BigBrain is slightly different or is it a genuine divergence between modalities? Of course addressing these questions is out of scope of this manuscript, but some discussion could be useful; I also think this toolbox may be useful for addressing this very concerns!

We agree that these are important questions and hope that BigBrainWarp will propel further research. Here, we consider these questions from two perspectives; the accuracy of the transformations and the potential influence of individual variation. For the former, we conducted a quantitative analysis on the accuracy of transformations used in BigBrainWarp (new Figure 2). We provide a function (evaluate_warp.sh) for BigBrainWarp users to assess accuracy of novel deformation fields and encourage detailed inspection of accuracy estimates and deformation effects for region of interest studies. For the latter, we expanded our Discussion of previous research on inter-individual variability and comment on the potential implications of unquantified inter-individual variability for the interpretation of BigBrain-MRI comparisons.

Methods (P.7-8):

“A prior study (Xiao et al., 2019) was able to further improve the accuracy of the transformation for subcortical structures and the hippocampus using a two-stage multi-contrast registration. The first stage involved nonlinear registration of BigBrainSym to a PD25 T1-T2 fusion atlas (Xiao et al., 2017, 2015), using manual segmentations of the basal ganglia, red nucleus, thalamus, amygdala, and hippocampus as additional shape priors. Notably, the PD25 T1-T2 fusion contrast is more similar to the BigBrainSym intensity contrast than a T1-weighted image. The second stage involved nonlinear registration of PD25 to ICBM2009sym and ICBM2009asym using multiple contrasts. The deformation fields were made available on Open Science Framework (https://osf.io/xkqb3/). The accuracy of the transformations was evaluated relative to overlap of region labels and alignment of anatomical fiducials (Lau et al., 2019). The two-stage procedure resulted in 0.86-0.97 Dice coefficients for region labels, improving upon direct overlap of BigBrainSym with ICBM2009sym (0.55-0.91 Dice) (Figure 2Aii, 2Aiv top). Transformed anatomical fiducials exhibited 1.77±1.25mm errors, on par with direct overlap of BigBrainSym with ICBM2009sym (1.83±1.47mm) (Figure 2Aiii, 2Aiv below). The maximum misregistration distance (BigBrainSym=6.36mm, Xiao=5.29mm) provides an approximation of the degree of uncertainty in the transformation. In line with this work, BigBrainWarp enables evaluation of novel deformation fields using anatomical fiducials and region labels (evaluate_warps.sh). The script accepts a nonlinear transformation file for registration of BigBrainSym to ICBM2009sym, or vice versa, and returns the Jacobian map, Dice coefficients for labelled regions and landmark misregistration distances for the anatomical fiducials.

The unique morphology of BigBrain also presents challenges for surface-based transformations. Idiosyncratic gyrification of certain regions of BigBrain, especially the anterior cingulate, cause misregistration (Lewis et al., 2020). Additionally, the areal midline representation of BigBrain, following inflation to a sphere, is disproportionately smaller than standard surface templates, which is related to differences in surface area, in hemisphere separation methods, and in tessellation methods. To overcome these issues, ongoing work (Lewis et al., 2020) combines a specialised BigBrain surface mesh with multimodal surface matching [MSM; (Robinson et al., 2018, 2014)] to co-register BigBrain to standard surface templates. In the first step, the BigBrain surface meshes were re-tessellated as unstructured meshes with variable vertex density (Möbius and Kobbelt, 2010) to be more compatible with FreeSurfer generated meshes. Then, coarse-to-fine MSM registration was applied in three stages. An affine rotation was applied to the BigBrain sphere, with an additional “nudge” based on an anterior cingulate landmark. Next, nonlinear/discrete alignment using sulcal depth maps (emphasising global scale, Figure 2Biii), followed by nonlinear/discrete alignment using curvature maps (emphasising finer detail, Figure 2Biii). The higher- order MSM procedure that was implemented for BigBrain maximises concordance of these features while minimising surface deformations in a physically plausible manner, accounting for size and shape distortions (Figure 2Bi) (Knutsen et al., 2010; Robinson et al., 2018). This modified MSMsulc+curv pipeline improves the accuracy of transformed cortical maps (4.38±3.25mm), compared to a standard MSMsulc approach (8.02±7.53mm) (Figure 2Bii-iii) (Lewis et al., 2020).”

Figure 2: Evaluating BigBrain-MRI transformations. A) Volume-based transformations i. Jacobian determinant of deformation field shown with a sagittal slice and stratified by lobe. Subcortical+ includes the shape priors (as described in Methods) and the + connotes hippocampus, which is allocortical. Lobe labels were defined based on assignment of CerebrA atlas labels (Manera et al., 2020) to each lobe. ii. Sagittal slices illustrate the overlap of native ICBM2009b and transformed subcortical+ labels. iii. Superior view of anatomical fiducials (Lau et al., 2019). iv. Violin plots show the DICE coefficient of regional overlap (ii) and landmark misregistration (iii) for the BigBrainSym and Xiao et al., approaches. Higher DICE coefficients shown improved registration of subcortical+ regions with Xiao et al., while distributions of landmark misregistration indicate similar performance for alignment of anatomical fiducials. B) Surface-based transformations. i. Inflated BigBrain surface projections and ridgeplots illustrate regional variation in the distortions of the mesh invoked by the modified MSMsulc+curv pipeline. ii. Eighteen anatomical landmarks shown on the inflated BigBrain surface (above) and inflated fsaverage (below). BigBrain landmarks were transformed to fsaverage using the modified MSMsulc+curv pipeline. Accuracy of the transformation was calculated on fsaverage as the geodesic distance between landmarks transformed from BigBrain and the native fsaverage landmarks. iii. Sulcal depth and curvature maps are shown on inflated BigBrain surface. Violin plots show the improved accuracy of the transformation using the modified MSMsulc+curv pipeline, compared to a standard MSMsulc approach.

Discussion (P.18):

“Cortical folding is variably associated with cytoarchitecture, however. The correspondence of morphology with cytoarchitectonic boundaries is stronger in primary sensory than association cortex (Fischl et al., 2008; Rajkowska and Goldman-Rakic, 1995a, 1995b). Incorporating more anatomical information in the alignment algorithm, such as intracortical myelin or connectivity, may benefit registration, as has been shown in neuroimaging (Orasanu et al., 2016; Robinson et al., 2018; Tardif et al., 2015). Overall, evaluating the accuracy of volume- and surface-based transformations is important for selecting the optimal procedure given a specific research question and to gauge the degree of uncertainty in a registration.”

Discussion (P.19):

“Despite all its promises, the singular nature of BigBrain currently prohibits replication and does not capture important inter-individual variation. While large-scale cytoarchitectural patterns are conserved across individuals, the position of areal boundaries relative to sulci vary, especially in association cortex (Amunts et al., 2020; Fischl et al., 2008; Zilles and Amunts, 2013) . This can affect interpretation of BigBrain-MRI comparisons. For instance, in tutorial 3, low predictive accuracy of functional communities by cytoarchitecture may be attributable to the subject- specific topographies, which are well established in functional imaging (Benkarim et al., 2020; Braga and Buckner, 2017; Gordon et al., 2017; Kong et al., 2019). Future studies should consider the influence of inter-subject variability in concert with the precision of transformations, as these two elements of uncertainty can impact our interpretations, especially at higher granularity.”

Reviewer #2:

This is a nice paper presenting a review of recent developments and research resulting from BigBrain and a tutorial guiding use of the BigBrainWarp toolbox. This toolbox supports registration to, and from, standard MRI volumetric and surface templates, together with mapping derived features between spaces. Examples include projecting histological gradients estimated from BigBrain onto fsaverage (and the ICMB2009 atlas) and projecting Yeo functional parcels onto the BigBrain atlas.

The key strength of this paper is that it supports and expands on a comprehensive tutorial and docker support available from the website. The tutorials there go into even more detail (with accompanying bash scripts) of how to run the full pipelines detailed in the paper. The docker makes the tool very easy to install but I was also able to install from source. The tutorials are diverse examples of broad possible applications; as such the combined resource has the potential to be highly impactful.

The minor weaknesses of the paper relate to its clarity and depth. Firstly, I found the motivations of the paper initially unclear from the abstract. I would recommend much more clearly stating that this is a review paper of recent research developments resulting from the BigBrain atlas, and a tutorial to accompany the bash scripts which apply the warps between spaces. The registration methodology is explained elsewhere.

In the revised Abstract (P.1), we emphasise that the manuscript involves a review of recent literature, the introduction of BigBrainWarp, and easy-to-follow tutorials to demonstrate its utility.

“Neuroimaging stands to benefit from emerging ultrahigh-resolution 3D histological atlases of the human brain; the first of which is “BigBrain”. Here, we review recent methodological advances for the integration of BigBrain with multi-modal neuroimaging and introduce a toolbox, “BigBrainWarp", that combines these developments. The aim of BigBrainWarp is to simplify workflows and support the adoption of best practices. This is accomplished with a simple wrapper function that allows users to easily map data between BigBrain and standard MRI spaces. The function automatically pulls specialised transformation procedures, based on ongoing research from a wide collaborative network of researchers. Additionally, the toolbox improves accessibility of histological information through dissemination of ready-to-use cytoarchitectural features. Finally, we demonstrate the utility of BigBrainWarp with three tutorials and discuss the potential of the toolbox to support multi-scale investigations of brain organisation.”

I also found parts of the paper difficult to follow - as a methodologist without comprehensive neuroanatomical terminology, I would recommend the review of past work to be written in a more 'lay' way. In many cases, the figure captions also seemed insufficient at first. For example it was not immediately obvious to me what is meant by 'mesiotemporal confluence' and Fig 1G is not referenced specifically in the text. In Fig 3C it is not immediately clear from the text of the caption that the cortical image is representing the correlation from the plots - specifically since functional connectivity is itself estimated through correlation.

In the updated manuscript, we have tried to remove neuroanatomical jargon and clearly define uncommon terms at the first instance in text. For example,

“Evidence has been provided that cortical organisation goes beyond a segregation into areas. For example, large- scale gradients that span areas and cytoarchitectonic heterogeneity within a cortical area have been reported (Amunts and Zilles, 2015; Goulas et al., 2018; Wang, 2020). Such progress became feasible through integration of classical techniques with computational methods, supporting more observer-independent evaluation of architectonic principles (Amunts et al., 2020; Paquola et al., 2019; Schiffer et al., 2020; Spitzer et al., 2018). This paves the way for novel investigations of the cellular landscape of the brain.”

“Using the proximal-distal axis of the hippocampus, we were able to bridge the isocortical and hippocampal surface models recapitulating the smooth confluence of cortical types in the mesiotemporal lobe, i.e. the mesiotemporal confluence (Figure 1G).”

“Here, we illustrate how we can track resting-state functional connectivity changes along the latero-medial axis of the mesiotemporal lobe, from parahippocampal isocortex towards hippocampal allocortex, hereafter referred to as the iso-to-allocortical axis.”

Additionally, we have expanded the captions for clarity. For example, Figure 3:

“C) Intrinsic functional connectivity was calculated between each voxel of the iso-to-allocortical axis and 1000 isocortical parcels. For each parcel, we calculated the product-moment correlation (r) of rsFC strength with iso-to- allocortical axis position. Thus, positive values (red) indicate that rsFC of that isocortical parcel with the mesiotemporal lobe increases along the iso-to-allocortex axis, whereas negative values (blue) indicate decrease in rsFC along the iso-to-allocortex axis.”

My minor concern is over the lack of details in relation to the registration pipelines. I understand these are either covered in previous papers or are probably destined for bespoke publications (in the case of the surface registration approach) but these details are important for readers to understand the constraints and limitations of the software. At this time, the details for the surface registration only relate to an OHBM poster and not a publication, which I was unable to find online until I went through the tutorial on the BigBrain website. In general I think a paper should have enough information on key techniques to stand alone without having to reference other publications, so, in my opinion, a high level review of these pipelines should be added here.

There isn't enough details on the registration. For the surface, what features were used to drive alignment, how was it parameterised (in particular the regularisation - strain, pairwise or areal), how was it pre-processed prior to running MSM - all these details seem to be in the excellent poster. I appreciate that work deserves a stand alone publication but some details are required here for users to understand the challenges, constraints and limitations of the alignment. Similar high level details should be given for the registration work.

We expanded descriptions of the registration strategies behind BigBrainWarp, especially so for the surface-based registration. Additionally, we created a new Figure to illustrate how the accuracy of the transformations may be evaluated.

Methods (P.7-8):

“For the initial BigBrain release (Amunts et al., 2013), full BigBrain volumes were resampled to ICBM2009sym (a symmetric MNI152 template) and MNI-ADNI (an older adult T1-weighted template) (Fonov et al., 2011). Registration of BigBrain to ICBM2009sym, known as BigBrainSym, involved a linear then a nonlinear transformation (available on ftp://bigbrain.loris.ca/BigBrainRelease.2015/). The nonlinear transformation was defined by a symmetric diffeomorphic optimiser [SyN algorithm, (Avants et al., 2008)] that maximised the cross- correlation of the BigBrain volume with inverted intensities and a population-averaged T1-weighted map in ICBM2009sym space. The Jacobian determinant of the deformation field illustrates the degree and direction of distortions on the BigBrain volume (Figure 2Ai top).

A prior study (Xiao et al., 2019) was able to further improve the accuracy of the transformation for subcortical structures and the hippocampus using a two-stage multi-contrast registration. The first stage involved nonlinear registration of BigBrainSym to a PD25 T1-T2 fusion atlas (Xiao et al., 2017, 2015), using manual segmentations of the basal ganglia, red nucleus, thalamus, amygdala, and hippocampus as additional shape priors. Notably, the PD25 T1-T2 fusion contrast is more similar to the BigBrainSym intensity contrast than a T1-weighted image. The second stage involved nonlinear registration of PD25 to ICBM2009sym and ICBM2009asym using multiple contrasts. The deformation fields were made available on Open Science Framework (https://osf.io/xkqb3/). The accuracy of the transformations was evaluated relative to overlap of region labels and alignment of anatomical fiducials (Lau et al., 2019). The two-stage procedure resulted in 0.86-0.97 Dice coefficients for region labels, improving upon direct overlap of BigBrainSym with ICBM2009sym (0.55-0.91 Dice) (Figure 2Aii, 2Aiv top). Transformed anatomical fiducials exhibited 1.77±1.25mm errors, on par with direct overlap of BigBrainSym with ICBM2009sym (1.83±1.47mm) (Figure 2Aiii, 2Aiv below). The maximum misregistration distance (BigBrainSym=6.36mm, Xiao=5.29mm) provides an approximation of the degree of uncertainty in the transformation. In line with this work, BigBrainWarp enables evaluation of novel deformation fields using anatomical fiducials and region labels (evaluate_warps.sh). The script accepts a nonlinear transformation file for registration of BigBrainSym to ICBM2009sym, or vice versa, and returns the Jacobian map, DICE coefficients for labelled regions and landmark misregistration distances for the anatomical fiducials.

The unique morphology of BigBrain also presents challenges for surface-based transformations. Idiosyncratic gyrification of certain regions of BigBrain, especially the anterior cingulate, cause misregistration (Lewis et al., 2020). Additionally, the areal midline representation of BigBrain, following inflation to a sphere, is disproportionately smaller than standard surface templates, which is related to differences in surface area, in hemisphere separation methods, and in tessellation methods. To overcome these issues, ongoing work (Lewis et al., 2020) combines a specialised BigBrain surface mesh with multimodal surface matching [MSM; (Robinson et al., 2018, 2014)] to co-register BigBrain to standard surface templates. In the first step, the BigBrain surface meshes were re-tessellated as unstructured meshes with variable vertex density (Möbius and Kobbelt, 2010) to be more compatible with FreeSurfer generated meshes. Then, coarse-to-fine MSM registration was applied in three stages. An affine rotation was applied to the BigBrain sphere, with an additional “nudge” based on an anterior cingulate landmark. Next, nonlinear/discrete alignment using sulcal depth maps (emphasising global scale, Figure 2Biii), followed by nonlinear/discrete alignment using curvature maps (emphasising finer detail, Figure 2Biii). The higher- order MSM procedure that was implemented for BigBrain maximises concordance of these features while minimising surface deformations in a physically plausible manner, accounting for size and shape distortions (Figure 2Bi) (Knutsen et al., 2010; Robinson et al., 2018). This modified MSMsulc+curv pipeline improves the accuracy of transformed cortical maps (4.38±3.25mm), compared to a standard MSMsulc approach (8.02±7.53mm) (Figure 2Bii-iii) (Lewis et al., 2020).”

(SEE FIGURE 2 in Response to Reviewer #1)

I would also recommend more guidance in terms of limitations relating to inter-subject variation. My interpretation of the results of tutorial 3, is that topographic variation of the cortex could easily be driving the greater variation of the frontal parietal networks. Either that, or the Yeo parcel has insufficient granularity; however, in that case any attempt to go to finer MRI driven parcellations - for example to the HCP parcellation, would create its own problems due to subject specific variability.

We agree that inter-individual variation may contribute to the low predictive accuracy of functional communities by cytoarchitecture. We expanded upon this possibility in the revised Discussion (P. 19) and recommend that future studies examine the uncertainty of subject-specific topographies in concert with uncertainties of transformations.

“These features depict the vast cytoarchitectural heterogeneity of the cortex and enable evaluation of homogeneity within imaging-based parcellations, for example macroscale functional communities (Yeo et al., 2011). The present analysis showed limited predictability of functional communities by cytoarchitectural profiles, even when accounting for uncertainty at the boundaries (Gordon et al., 2016). [...] Despite all its promises, the singular nature of BigBrain currently prohibits replication and does not capture important inter-individual variation. While large- scale cytoarchitectural patterns are conserved across individuals, the position of boundaries relative to sulci vary, especially in association cortex (Amunts et al., 2020; Fischl et al., 2008; Zilles and Amunts, 2013) . This can affect interpretation of BigBrain-MRI comparisons. For instance, in tutorial 3, low predictive accuracy of functional communities by cytoarchitecture may be attributable to the subject-specific topographies, which are well established in functional imaging (Benkarim et al., 2020; Braga and Buckner, 2017; Gordon et al., 2017; Kong et al., 2019). Future studies should consider the influence of inter-subject variability in concert with the precision of transformations, as these two elements of uncertainty can impact our interpretations, especially at higher granularity.”

Reviewer #3:

The authors make a point for the importance of considering high-resolution, cell-scale, histological knowledge for the analysis and interpretation of low-resolution MRI data. The manuscript describes the aims and relevance of the BigBrain project. The BigBrain is the whole brain of a single individual, sliced at 20µ and scanned at 1µ resolution. During the last years, a sustained work by the BigBrain team has led to the creation of a precise cell-scale, 3D reconstruction of this brain, together with manual and automatic segmentations of different structures. The manuscript introduces a new tool - BigBrainWarp - which consolidates several of the tools used to analyse BigBrain into a single, easy to use and well documented tool. This tool should make it easy for any researcher to use the wealth of information available in the BigBrain for the annotation of their own neuroimaging data. The authors provide three examples of utilisation of BigBrainWarp, and show the way in which this can provide additional insight for analysing and understanding neuroimaging data. The BigBrainWarp tool should have an important impact for neuroimaging research, helping bridge the multi-scale resolution gap, and providing a way for neuroimaging researchers to include cell-scale phenomena in their study of brain data. All data and code are available open source, open access.

Main concern:

One of the longstanding debates in the neuroimaging community concerns the relationship between brain geometry (in particular gyro/sulcal anatomy) and the cytoarchitectonic, connective and functional organisation of the brain. There are various examples of correspondance, but also many analyses showing its absence, particularly in associative cortex (for example, Fischl et al (2008) by some of the co-authors of the present manuscript). The manuscript emphasises the accuracy of their transformations to the different atlas spaces, which may give some readers a false impression. True: towards the end of the manuscript the authors briefly indicate the difficulty of having a single brain as source of histological data. I think, however, that the manuscript would benefit from making this point more clearly, providing the future users of BigBrainWarp with some conceptual elements and references that may help them properly apprise their results. In particular, it would be helpful to briefly describe which aspects of brain organisation where used to lead the deformation to the different templates, if they were only based on external anatomy, or if they took into account some other aspects such as myelination, thickness, …

We agree with the Reviewer that the accuracy of the transformation and the potential influence of inter-individual variability should be carefully considered in BigBrain-MRI studies. To highlight these issues in the updated manuscript, we first conducted a quantitative analysis on the accuracy of transformations used in BigBrainWarp (new Figure 2). We provide a function (evaluate_warp.sh) for users to assess accuracy of novel deformation fields and encourage detailed inspection of accuracy estimates and deformation effects for region of interest studies. Second, we expanded our discussion of previous research on inter-individual variability and comment on the potential implications of unquantified inter-individual variability for the interpretation of BigBrain-MRI comparisons.

Methods (P.7-8):

“A prior study (Xiao et al., 2019) was able to further improve the accuracy of the transformation for subcortical structures and the hippocampus using a two-stage multi-contrast registration. The first stage involved nonlinear registration of BigBrainSym to a PD25 T1-T2 fusion atlas (Xiao et al., 2017, 2015), using manual segmentations of the basal ganglia, red nucleus, thalamus, amygdala, and hippocampus as additional shape priors. Notably, the PD25 T1-T2 fusion contrast is more similar to the BigBrainSym intensity contrast than a T1-weighted image. The second stage involved nonlinear registration of PD25 to ICBM2009sym and ICBM2009asym using multiple contrasts. The deformation fields were made available on Open Science Framework (https://osf.io/xkqb3/). The accuracy of the transformations was evaluated relative to overlap of region labels and alignment of anatomical fiducials (Lau et al., 2019). The two-stage procedure resulted in 0.86-0.97 Dice coefficients for region labels, improving upon direct overlap of BigBrainSym with ICBM2009sym (0.55-0.91 Dice) (Figure 2Aii, 2Aiv top). Transformed anatomical fiducials exhibited 1.77±1.25mm errors, on par with direct overlap of BigBrainSym with ICBM2009sym (1.83±1.47mm) (Figure 2Aiii, 2Aiv below). The maximum misregistration distance (BigBrainSym=6.36mm, Xiao=5.29mm) provides an approximation of the degree of uncertainty in the transformation. In line with this work, BigBrainWarp enables evaluation of novel deformation fields using anatomical fiducials and region labels (evaluate_warps.sh). The script accepts a nonlinear transformation file for registration of BigBrainSym to ICBM2009sym, or vice versa, and returns the Jacobian map, Dice coefficients for labelled regions and landmark misregistration distances for the anatomical fiducials.

The unique morphology of BigBrain also presents challenges for surface-based transformations. Idiosyncratic gyrification of certain regions of BigBrain, especially the anterior cingulate, cause misregistration (Lewis et al., 2020). Additionally, the areal midline representation of BigBrain, following inflation to a sphere, is disproportionately smaller than standard surface templates, which is related to differences in surface area, in hemisphere separation methods, and in tessellation methods. To overcome these issues, ongoing work (Lewis et al., 2020) combines a specialised BigBrain surface mesh with multimodal surface matching [MSM; (Robinson et al., 2018, 2014)] to co-register BigBrain to standard surface templates. In the first step, the BigBrain surface meshes were re-tessellated as unstructured meshes with variable vertex density (Möbius and Kobbelt, 2010) to be more compatible with FreeSurfer generated meshes. Then, coarse-to-fine MSM registration was applied in three stages. An affine rotation was applied to the BigBrain sphere, with an additional “nudge” based on an anterior cingulate landmark. Next, nonlinear/discrete alignment using sulcal depth maps (emphasising global scale, Figure 2Biii), followed by nonlinear/discrete alignment using curvature maps (emphasising finer detail, Figure 2Biii). The higher- order MSM procedure that was implemented for BigBrain maximises concordance of these features while minimising surface deformations in a physically plausible manner, accounting for size and shape distortions (Figure 2Bi) (Knutsen et al., 2010; Robinson et al., 2018). This modified MSMsulc+curv pipeline improves the accuracy of transformed cortical maps (4.38±3.25mm), compared to a standard MSMsulc approach (8.02±7.53mm) (Figure 2Bii-iii) (Lewis et al., 2020).”

(SEE Figure 2 in response to previous reviewers)

Discussion (P.18, 19):

“Cortical folding is variably associated with cytoarchitecture, however. The correspondence of morphology with cytoarchitectonic boundaries is stronger in primary sensory than association cortex (Fischl et al., 2008; Rajkowska and Goldman-Rakic, 1995a, 1995b). Incorporating more anatomical information in the alignment algorithm, such as intracortical myelin or connectivity, may benefit registration, as has been shown in neuroimaging (Orasanu et al., 2016; Robinson et al., 2018; Tardif et al., 2015). Overall, evaluating the accuracy of volume- and surface-based transformations is important for selecting the optimal procedure given a specific research question and to gauge the degree of uncertainty in a registration.”

“Despite all its promises, the singular nature of BigBrain currently prohibits replication and does not capture important inter-individual variation. While large-scale cytoarchitectural patterns are conserved across individuals, the position of boundaries relative to sulci vary, especially in association cortex (Amunts et al., 2020; Fischl et al., 2008; Zilles and Amunts, 2013) . This can have implications on interpretation of BigBrain-MRI comparisons. For instance, in tutorial 3, low predictive accuracy of functional communities by cytoarchitecture may be attributable to the subject-specific topographies, which are well established in functional imaging (Benkarim et al., 2020; Braga and Buckner, 2017; Gordon et al., 2017; Kong et al., 2019). Future studies should consider the influence of inter- subject variability in concert with the precision of transformations, as these two elements of uncertainty can impact our interpretations, especially at higher granularity.”

Minor:

1) In the abstract and later in p9 the authors talk about "state-of-the-art" non-linear deformation matrices. This may be confusing for some readers. To me, in brain imaging a matrix is most often a 4x4 affine matrix describing a linear transformation. However, the authors seem to be describing a more complex, non-linear deformation field. Whereas building a deformation matrix (4x4 affine) is not a big challenge, I agree that more sophisticated tools should provide more sophisticated deformation fields. The authors may consider using "deformation field" instead of "deformation matrix", but I leave that to their judgment.

As suggested, we changed the text to “deformation field” where relevant.

2) In the results section, p11, the authors highlight the challenge of segmenting thalamic nuclei or different hippocampal regions, and suggest that this should be simplified by the use of the histological BigBrain data. However, the atlases currently provided in the OSF project do not include these more refined parcellation: there's one single "Thalamus" label, and one single "Hippocampus" label (not really single: left and right). This could be explicitly stated to prevent readers from having too high expectations (although I am certain that those finer parcellations should come in the very close future).

We updated the text to reflect the current state of such parcellations. While subthalamic nuclei are not yet segmented (to our knowledge), one of the present authors has segmented hippocampal subfields (https://osf.io/bqus3/) and we highlight this in the Results (P.11-12):

“Despite MRI acquisitions at high and ultra-high fields reaching submillimeter resolutions with ongoing technical advances, certain brain structures and subregions remain difficult to identify (Kulaga-Yoskovitz et al., 2015; Wisse et al., 2017; Yushkevich et al., 2015). For example, there are challenges in reliably defining the subthalamic nucleus (not yet released for BigBrain) or hippocampal Cornu Ammonis subfields [manual segmentation available on BigBrain, https://osf.io/bqus3/, (DeKraker et al., 2019)]. BigBrain-defined labels can be transformed to a standard imaging space for further investigation. Thus, this approach can support exploration of the functional architecture of histologically-defined regions of interest.”

Author Response:

Reviewer #2 (Public Review):

Summary:

Frey et al develop an automated decoding method, based on convolutional neural networks, for wideband neural activity recordings. This allows the entire neural signal (across all frequency bands) to be used as decoding inputs, as opposed to spike sorting or using specific LFP frequency bands. They show improved decoding accuracy relative to standard Bayesian decoder, and then demonstrate how their method can find the frequency bands that are important for decoding a given variable. This can help researchers to determine what aspects of the neural signal relate to given variables.

Impact:

I think this is a tool that has the potential to be widely useful for neuroscientists as part of their data analysis pipelines. The authors have publicly available code on github and Colab notebooks that make it easy to get started using their method.

Relation to other methods:

This paper takes the following 3 methods used in machine learning and signal processing, and combines them in a very useful way. 1) Frequency-based representations based on spectrograms or wavelet decompositions (e.g. Golshan et al, Journal of Neuroscience Methods, 2020; Vilamala et al, 2017 IEEE international workshop on on machine learning for signal processing). This is used for preprocessing the neural data; 2) Convolutional neural networks (many examples in Livezey and Glaser, Briefings in Bioinformatics, 2020). This is used to predict the decoding output; 3) Permutation feature importance, aka a shuffle analysis (https://scikit-learn.org/stable/modules/permutation_importance.htmlhttps://compstat-lmu.github.io/iml_methods_limitations/pfi.html). This is used to determine which input features are important. I think the authors could slightly improve their discussion/referencing of the connection to the related literature.

Overall, I think this paper is a very useful contribution, but I do have a few concerns, as described below.

We thank the reviewer for the encouraging feedback and the helpful summary of the approaches we used. We are happy to read that they consider the framework to be a very useful contribution to the field of neuroscience. The reviewer raises several important questions regarding the influence measure/feature importance, the data format of the SVM and how the model can be used on EEG/ECoG datasets. Moreover, they suggest clarifying the general overview of the approach and to connect it more to the related literature. These are very helpful and thoughtful comments and we are grateful to be given the opportunity to address them.

Concerns:

1) The interpretability of the method is not validated in simulations. To trust that this method uncovers the true frequency bands that matter for decoding a variable, I feel it's important to show the method discovers the truth when it is actually known (unlike in neural data). As a simple suggestion, you could take an actual wavelet decomposition, and create a simple linear mapping from a couple of the frequency bands to an imaginary variable; then, see whether your method determines these frequencies are the important ones. Even if the model does not recover the ground truth frequency bands perfectly (e.g. if it says correlated frequency bands matter, which is often a limitation of permutation feature importance), this would be very valuable for readers to be aware of.

2) It's unclear how much data is needed to accurately recover the frequency bands that matter for decoding, which may be an important consideration for someone wanting to use your method. This could be tested in simulations as described above, and by subsampling from your CA1 recordings to see how the relative influence plots change.

We thank the reviewer for this really interesting suggestion to validate our model using simulations. Accordingly, we have now trained our model on simulated behaviours, which we created via linear mapping to frequency bands. As shown in Figure 3 - Supplement 2B, the frequency bands modulated by the simulated behaviour can be clearly distinguished from the unmodulated frequency bands. To make the synthetic data more plausible we chose different multipliers (betas) for each frequency component which explains the difference between the peak at 58Hz (beta = 2) and the peak at 3750Hz (beta = 1).

To generate a more detailed understanding of how the detected influence of a variable changes based on the amount of data available, we conducted an additional analysis. Using the real data, we subsampled the training data from 1 to 35 minutes and fully retrained the model using cross-validation. We then used the original feature importance implementation to calculate influence scores across each cross-validation split. To quantify the similarity between the original influence measure and the downsampled influence we calculated the Pearson correlation between the downsampled influence and the one obtained when using the full training set. As can be seen in Figure 3 - Supplement 2A our model achieves an accurate representation of the true influence with as little as 5 minutes of training data (mean Pearson's r = 0.89 ± 0.06)

Page 8-9: To further assess the robustness of the influence measure we conducted two additional analyses. First, we tested how results depended on the amount of training data - (1 - 35 minutes, see Methods). We found that our model achieves an accurate representation of the true influence with as little as 5 minutes of training data (mean Pearson's r = 0.89 ± 0.06, Figure 3 - Supplement 2A). Secondly, we assessed influence accuracy on a simulated behaviour in which we varied the ground truth frequency information (see Methods). The model trained on the simulated behaviour is able to accurately represent the ground truth information (modulated frequencies 58 Hz & 3750 Hz, Figure 3 - Supplement 2B)

Page 20: To evaluate if the influence measure accurately captures the true information content, we used simulated behaviours in which ground truth information was known. We used the preprocessed wavelet transformed data from one animal and created a simulated behaviour ysb using uniform random noise. Two frequency bands were then modulated by the simulated behaviour using fnew = fold * β * ysb. We used β=2 for 58Hz and β=1 for 3750Hz. We then retrained the model using five-fold cross validation and evaluated the influence measure as previously described. We report the proportion of frequency bands that fall into the correct frequencies (i.e. the frequencies we chose to be modulated, 58 Hz & 3750 Hz).

New supplementary Figure:

Figure 3 - Supplement 2: Decoding influence for downsampled models and simulations. (A) To measure the robustness of the influence measure we downsampled the training data and retrained the model using cross-validation. We plot the Pearson correlation between the original influence distribution using the full training set and the influence distribution obtained from the downsampled data. Each dot shows one cross-validation split. Inset shows influence plots for two runs, one for 35 minutes of training data, the other in which model training consisted of only 5 minutes of training data. (B) We quantified our influence measure using simulated behaviours. We used the wavelet preprocessed data from one CA1 recording and simulated two behavioural variables which were modulated by two frequencies (58Hz & 3750Hz) using different multipliers (betas 2 & 1). We then trained the model using cross-validation and calculated the influence scores via feature shuffling.

3)

a) It is not clear why your method leads to an increase in decoding accuracy (Fig. 1)? Is this simply because of the preprocessing you are using (using the Wavelet coefficients as inputs), or because of your convolutional neural network. Having a control where you provide the wavelet coefficients as inputs into a feedforward neural network would be useful, and a more meaningful comparison than the SVM. Side note - please provide more information on the SVM you are using for comparison (what is the kernel function, are you using regularization?).

We thank the reviewer for this suggestion and are sorry for the lack of documentation regarding the support vector machine model. The support vector machine was indeed trained on the wavelet transformed data and not on the spike sorted data as we wanted a comparison model which also uses the raw data. The high error of the support vector machine on wavelet transformed data might stem from two problems: (1) The input by design loses all spatial relevant information as the 3-D representation (frequencies x channels x time) needs to be flattened into a 1-D vector in order to train an SVM on it and (2) the SVM therefore needs to deal with a huge number of features. For example, even though the wavelets are downsampled to 30Hz, one sample still consists of (64 timesteps * 128 channels * 26 frequencies) 212992 features, which leads the SVM to be very slow to train and to an overfit on the training set.

This exact problem would also be present in a feedforward neural network that uses the wavelet coefficients as input. Any hidden layer connected to the input, using a reasonable amount of hidden units will result in a multi-million parameter model (e.g. 512 units will result in 109051904 parameters for just the first layer). These models are notoriously hard to train and won’t fit many consumer-grade GPUs, which is why for most spatial signals including images or higher-dimensional signals, convolutional layers are the preferred and often only option to train these models.

We have now included more detailed information about the SVM (including kernel function and regularization parameters) in the methods section of the manuscript.

Page 19:To generate a further baseline measure of performance when decoding using wavelet transformed coefficients, we trained support vector machines to decode position from wavelet transformed CA1 recordings. We used either a linear kernel or a non-linear radial-basis-function (RBF) kernel to train the model, using a regularization factor of C=100. For the non-linear RBF kernel we set gamma to the default 1 / (num_features * var(X)) as implemented in the sklearn framework. The SVM model was trained on the same wavelet coefficients as the convolutional neural network

b) Relatedly, because the reason for the increase in decoding accuracy is not clear, I don't think you can make the claim that "The high accuracy and efficiency of the model suggest that our model utilizes additional information contained in the LFP as well as from sub-threshold spikes and those that were not successfully clustered." (line 122). Based on the shown evidence, it seems to me that all of the benefits vs. the Bayesian decoder could just be due to the nonlinearities of the convolutional neural network.

Thanks for raising this interesting point regarding the linear vs. non-linear information contained in the neural data. Indeed, when training the model with a linear activation function for the convolutions and fully connected layers, model performance drops significantly. To quantify this we ran the model with three different configurations regarding its activation functions. We (1) used nonlinear activation functions only in the convolutional layers (2) or the fully connected layers or (3) only used linear activation functions throughout the whole model. As expected the model with only linear activation functions performed the worst (linear activation functions 61.61cm ± 33.85cm, non-linear convolutional layers 22.99cm ± 18.67cm, non-linear fully connected layers 47.03cm ± 29.61cm, all layers non-linear 18.89cm ± 4.66cm). For comparison the Bayesian decoder achieves a decoding accuracy of 23.25cm ± 2.79cm on this data.

Thus it appears that the reviewer is correct - the advantage of the CNN model comes in part from the non-linearity of the convolutional layers. The corollary of this is that there are likely non-linear elements in the neural data that the CNN but not Bayes decoder can access. However, the CNN does also receive wider-band inputs and thus has the potential to utilize information beyond just detected spikes.

In response to the reviewers point and to the new analysis regarding the LFP models raised by reviewer 1, we have now reworded this sentence in the manuscript.

Page 4: The high accuracy and efficiency of the model for these harder samples suggest that the CNN utilizes additional information from sub-threshold spikes and those that were not successfully clustered, as well as nonlinear information which is not available to the Bayesian decoder.

Author Response

Reviewer #2 (Public Review):

Portes et al. investigated the nanoscale architecture and dynamics of the osteoclast sealing zone using high-end microscopy techniques. They first use DONALD 3D single molecule localization microscopy on osteoclasts seeded on glass to study the lateral and axial localization of key components of the sealing zone. They show that for some components (vinculin, talin Cterminus), the axial localization was higher when molecules were in close proximity to the actin core while for other components (cortactin, actinin, filamin, paxillin), there was no difference in height as a function of distance from the actin core. They next show that random illumination microscopy (RIM) is a suited microscopy technique to study the sealing zone of osteoclasts on a bone mimetic substrate. They continue to use RIM to show that the dynamics of neighbouring podosomes correlate up to a distance of about 1.5um. They next show that within the sealing zone, groups of podosomes are surrounded by the classical adhesion adaptor proteins such as vinculin, talin and paxillin while actinin is present at the periphery of all single cores. This suggests that the sealing zone has an "intermediate" level of organization and that groups of podosomes form a functional unit within the sealing zone. The authors lastly demonstrate that the fluorescence intensity of the cores within these groups correlate with the intensity of the adaptor proteins that surrounds the group and that also the fluorescence intensity of the cores within one group correlates with each other.

Strengths:

The authors use bone slices to evaluate the nanoscale organization of cytoskeletal components in the sealing zone. Podosome conformations in osteoclasts strongly depend on the substrate type and the usage of bone slices accurately mimics the physiological environment in which osteoclasts reside in vivo.

The authors use state-of-the-art imaging approaches to evaluation the nanoscale organization and dynamics of multiple podosome components in the sealing zone.

The identification of groups of podosomes that demonstrate correlated dynamics within the sealing zone is a novel finding that is convincingly demonstrated.

We thank the reviewer for these encouraging comments and the valuable suggestions below.

Weaknesses:

The rationale for the analysis performed on the DONALD super-resolution images (explained in Figure S1) is unclear. The analysis is also not properly explained and it is unclear how the data should be interpreted or put into context. Specific comments related to this analysis:

– The authors make a distinction between towards the internal or external part of the cell when it comes to the height of the investigated proteins but it is unclear why this is done. Also, while the authors make this distinction, no conclusions are derived from this distinction and only the height values from towards the internal part of the cell are mentioned in the text.

As the sealing zone is usually located near the cell periphery, we wondered whether the proximity of the peripheral plasma membrane could influence the molecular architecture of the structure, and a possible difference in tension between the inner and outer parts, and this is why we distinguished between the inner and outer side of the structures. However, our analyses revealed little difference between these two sides, the most striking being a closer proximity of the vinculin to the cores on the outer side of the belt. We now make this explicit in the manuscript (P3, L113116).

• It is very much unclear how the distance of the investigated proteins towards the actin core is calculated. From Figure S1, it seems like a rectangle is taken that is centered around a podosome but the rectangle in the example contains more than one core. It seems like this would influence a proper interpretation of the data presented in the figures than contain the height values. The authors should better explain how the analysis was performed and how the analysis deals with the presence of multiple podosome cores in the rectangle of interest.

We apologize for this omission. In order not to bias the analysis, the protein distance was calculated for all cores present, not just one. This is now specified in the legend of the figure.

• In the text, the distance of the proteins with respect to the actin core is given (350nm-710nm depending on the specific protein and localization towards the external or internal part of the cell). It is mentioned that the measurements are not shown but it should be better explained how these numbers were derived from the data and the measurements (average, SD/SEM) should be shown.

These values correspond to the maxima of the distributions of the different podosome markers shown in Figure 1G. Each of these proteins (vinculin, talin, filamin-A and paxillin) has a broad distribution marked by a depletion at the core, and not a peak as suggested by the first version of the manuscript. We propose not to indicate these values in the revised version in order to simplify the manuscript and not to confuse the reader.

• Related to the previous comment. While it is mentioned that vinculin for example is located at ~500nm from the actin core, the height values (Figure 1E) are binned within 50nm of the core. This does not seem to match. It would be very helpful if the authors would add how many localizations are found so close to the core. Since this is expected to be low it would also be valuable it the authors would discuss what this means for difference in height between the molecules found close by and away from the core.

Indeed, as shown in Figure 1G, vinculin is much less present in the center of actin cores than at 500 nm from these cores. The graph shown in Figure 1E, which shows the height of vinculin as a function of the distance to the core, without explaining the proportion of molecules detected, can indeed be confusing. This being said, a large number of molecules were detected, 197967 for the vinculin graph, including 5973 within 300 nm around the core, which is far from being negligible. To facilitate the understanding of this graph, as well as that of the graphs corresponding to the heights of the other proteins studied (Figures 1 and S2), we now superimpose on the height distributions, the frequency of the locations (new Figure 1E,F), still compiled in Figure 1G.

• For cortactin, filamin A and actinin it is found that they reside on average at a height of approximately 150nm, even up to a large distance from the podosome core. It is unclear how these values should be interpreted. 150nm is way above the location where actin is expected to be (and also way above the average actin height that is found by the authors, with approximately 80nm more distant from the cores). The authors should add a discussion of what type of structures cortactin, filamin A and actinin would associate to at this position or how this height can be explained. This should also be included in the final model of Figure 6. In the current cartoon, filamin A for example seems to be associated with the integrins but this does not match with the height position observed by the authors.

The average heights of cortactin, filamin-A and actinin are indeed around 150 nm, but are actually present over a wider range of heights (0-400nm), as shown in the histograms in Figure 1H. These values are therefore not inconsistent with the distribution of actin, which indeed has a lower average height, but is also present over this entire height (histogram now added in Figure 1H). These analyses suggest that there are different sets of actin filaments and that there is proportionally more cortactin, filamin-A and actinin on the high actin filaments, rather than on those close to the plasma membranes. To fully account for these results, we now point out the potential presence of different sets of actin filaments in the discussion (P7, L266-275) and corrected the model shown in the new Figure 6, placing a population of filamin A on the radial filaments, not just associated with integrins, and added filamin A and actinin in the side view of the model, to appreciate their likely localisation.

The authors mention that the RIM resolution is 100nm and 300nm in the lateral and axial direction, respectively. This should also be confirmed on the bone slices with beads. It is well conceivable that the optical properties of bone have an effect on the optimal RIM resolution.

In order to evaluate RIM resolution on osteoclast samples, as suggested by the reviewer, we did some experiments with beads and used the Fourier Ring Correlation Method (Nieuwenhuizen et al., Nat Methods 2013). This consists in making two RIM images with two different speckle illumination sequences, and comparing the correlations of the images in the Fourier space. The following figure shows the correlation curve as a function of spatial frequencies. The FIRE number, when the FRC curve reaches a correlation value of 1/7, gives an estimation of the resolution of the image.

Using this approach, we evaluated the resolution to be of 125 nm, in average.

The authors find three specific fluctuation periods (100s/25s/7s) but it is unclear what these periods mean. The authors only very briefly mention that these periods correlate with similar observations in macrophages but they should also add the implications of this finding and suggested a possible molecular mechanism that underlies these different fluctuations.

We agree with this comment. So far, the mechanisms regulating these oscillations, whether purely mechanical or involving signaling, as well as and their importance for podosome and sealing zone function, are not yet understood. In van den Dries et al. Nat Commun 2013 and Labernadie et al. Nat Commun 2014, it was shown that these oscillations in macrophage podosomes depend on myosin IIA activity. It would thus be interesting to explore the effects of drugs interfering with actin polymerization on both the periodicity and the spatial synchrony properties of the sealing zone. We now discuss this point in the manuscript (P7, L296-300).

The authors find that actinin-1 is localized around the podosome cores while filamin and vinculin surround groups of podosomes. The current representative images, though, that are chosen to support this difference display a very different density in podosome cores. The filamin and vinculin images seems to have a much denser podosome content compare to the actinin and cortactin images. I would encourage the authors to select images that are more comparable to fully appreciate the difference in localization of the associated proteins.

This is a good point. Indeed, not all sealing zones are alike, especially with respect to the density of actin cores. This is why we have chosen to show a gallery of different cases (now in Figure S7), and not to intentionally select always the same patterns in the main figures in order not to mislead the reader. It is important to note that whatever the actin density, we find the same locations for the different proteins.

In Figure 4 and 5, the authors show that the sealing zone is subdivided in groups of podosomes and it is implied that these for functional units within the sealing zone. Yet, it is unclear how persistent these groups are. Considering the dynamic nature of podosomes in other cell types (and as also demonstrated in the supplementary movies) it is well conceivable that these groups continuously fuse and remodel. To better define the nature of these groups of podosomes, the authors should add an analysis on these podosome groups and measure parameters such as group stability, podosome number per group, group size etc. This would very much enhance the novel aspects of the findings in this paper.

Following the reviewer’s suggestion, we have quantified the number of podosomes per group and the group size. Measurements of these islets of clustered cores showed that they were 2.3 +/-2.1 µm² (average +/-SD) and contained in 7 +/-8 (average +/-SD) cores. These results are now included in the manuscript (P6, L213). Unfortunately, we could not accurately measure the stability of the clusters, as this would require a long, and challenging, time-lapse by RIM of osteoclasts expressing both paxillin-GFP and lifeact-mCherry, which we were able to achieve only on a few cells and on short timescales.

The authors mention in the discussion that their finding about the groups of podosomes is very different from the "double circle" distribution found in previous publications. Yet, it is unclear what explains these different observations. While the authors use RIM super-resolution in this paper to assess the localization of the adaptor proteins, it is very unlikely that this is the source of this difference since the groups of podosomes would have been easily identified by conventional or confocal microscopy as well. The authors should add an extended discussion on how these differences could be explained and what this means for bone resorption properties.

Indeed, our observation that the sealing zone is composed of islets of actin cores that are bordered by a network of adhesion complexes diverge from most of the previous studies describing a “double circle” organization. We believe that this difference may come, not only from the high resolution of our images, but mainly from the fact that most studies on the organization of sealing zones have been performed on mouse osteoclasts. We also believe that this particular organisation probably allows an efficient sealing of the osteoclast plasma membrane to the bone surface and maintains the resorption lacuna and the diffusion barrier. We now indicate this in the discussion (L7, P286-288).

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:

Salehinejad et al. run a battery of tests to investigate the effects of sleep deprivation on cortical excitability using TMS, LTP/LTD-like plasticity using tDCS, EEG-derived measures and behavioral task-performance. The study confirms evidence for sleep deprivation resulting in an increase in cortical excitability, diminishing LTP-like plasticity changes, increase in EEG theta band-power and worse task-performance. Additionally, a protocol usual resulting in LTD-like plasticity results in LTP-like changes in the sleep deprivation condition.

We appreciate the reviewer's time for carefully reading our work and providing important suggestions/recommendations. In what follows, we addressed the comments one by one, revised the main text accordingly, and pasted the changes here as well.

1) My main comment is regarding the motivation for executing this specific study setup, which did not become clear to me. It's a robust experimental design, with general approach quite similar to the (in the current manuscript heavily cited) Kuhn et al. 2016 study (which investigates cortical excitability, EEG markers, and changes in LTP mechanisms), with additional inclusion of LTD-plasticity measures. The authors list comprehensiveness as motivation, but the power of a comprehensive study like this would lie in being able to make comparisons across measures to identify new interrelations or interesting subgroups of participants differentially affected by sleep deprivations. These comparisons are presented in l. 322 and otherwise at the end of the supplementary material and the study does not seem to be designed with these as the main motivation in mind. Can the authors could comment on this & clarify their motivation? Maybe the authors can highlight in what way their study constitutes a methodological improvement and incorporates new aspects regarding hypothesis development as compared to e.g. Kuhn et al. 2016; currently, the authors highlight mainly the addition of LTD-plasticity protocols. Similarly, no motivation/context/hypotheses are given for saliva testing. There are a lot of different results, but e.g. the cortical excitability results are not discussed in depth, e.g. there is no effect on IO curve, but on other measures of excitability, the conclusion of that paragraph is only "our results demonstrate that corticocortical and corticospinal excitability are upscaled after sleep deprivation." There are some conflicting results regarding cortical excitability measures in the literature, possibly this could be discussed, so the reader can evaluate in what way the current study constitutes an improvement, for instance methodologically, over previous studies.

Thank you for your comment/suggestion. The main motivation behind this study was to examine different physiological/behavioral/cognitive measures under sleep conditions and to provide a reasonably complete overview. This approach was not covered in detail by previous work, which is often limited to one or two pieces of behavioral and/or physiological evidence. Our study was not sufficiently powered to identify new interrelations between measures, because this was a secondary aim, although we found some relevant associations in exploratory analyses (i.e., association of motor learning with plasticity, and cortical excitability with memory and attention). Future studies, however, which are sufficiently powered for these comparisons, are needed to explore interrelations between physiological, and cognitive parameters more clearly and we stated this as a limitation (Page 22).

That said, we agree that specific rationales of the study were not sufficiently clarified in the previous version. We rephrased and clarified respective motivations and rationales here:

1) By comprehensive, we mean that we obtained measures from basic physiological parameters to behavior and higher-order cognition, which is not sufficiently covered so far. This includes also the exploration of expected associations between behavioral motor learning and plasticity measures, as well as excitability parameters and cognitive functions.

2) In the Kuhn et al. (2016) study, cortical excitability was obtained by TMS intensity (single- pulse protocol) to elicit a predefined amplitude of the motor-evoked potential, which is a relatively unspecific parameter of corticospinal excitability. In the present study, cortical excitability was monitored by different TMS protocols, which cover not only corticospinal excitability, but also intracortical inhibition, facilitation, I-wave facilitation, and short-latency afferent inhibition, which allow more specific conclusions with respect to the involvement of cortical systems, neurotransmitters, and -modulators.

3) Furthermore, Kuhn et al (2016) only investigated LTP-like, but not LTD-like plasticity. LTD- like plasticity was also not investigated in previous works to the best of our knowledge. LTD- like plasticity has however relevance for cognitive processing, and furthermore, knowledge about alterations of this kind of plasticity is important for mechanistic understanding of sleep- dependent plasticity alterations: The conversion of LTD-like to LTP-like plasticity under sleep deprivation is crucial for the interpretation of the study results as likely caused by cortical hyperactivity.

4) Finally, an important motivation was to compare how brain physiology and cognition are differently affected by sleep deprivation, as compared to chronotype-dependent brain physiology, and cognitive performance, especially with respect to brain physiology, and performance at non-preferred times of the day. Our findings regarding the latter were recently published (Salehinejad et al., 2021) and comparisons of the present study with the published one have a novel, and important implications. Specifically, the results of both studies imply that the mechanistic background of sleep deprivation-, and non-optimal time of day performance- dependent reduced performance differs relevantly.

We clarified these motivations in the introduction and discussion. Please see the revised text below:

"The number of available studies about the impact of sleep deprivation on human brain physiology relevant for cognitive processes is limited, and knowledge is incomplete. With respect to cortical excitability, Kuhn et al. (2016) showed increased excitability under sleep deprivation via a global measure of corticospinal excitability, the TMS intensity needed to induce motor-evoked potentials of a specific amplitude. Specific information about the cortical systems, including neurotransmitters, and - modulators involved in these effects (e.g. glutamatergic, GABAergic, cholinergic), is however missing. The level of cortical excitability affects neuroplasticity, a relevant physiological derivate of learning, and memory formation. Kuhn and co-workers (2016) describe accordingly a sleep deprivation-dependent alteration of LTP-like plasticity in humans. The effects of sleep deprivation on LTD-like plasticity, which is required for a complete picture, have however not been explored so far. In the present study, we aimed to complete the current knowledge and explored also cognitive performance on those tasks which critically depend on cortical excitability (working memory, and attention), and neuroplasticity (motor learning) to gain mechanistic knowledge about sleep deprivation-dependent performance decline. Finally, we aimed to explore if the impact of sleep deprivation on brain physiology and cognitive performance differs from the effects of non-optimal time of day performance in different chronotypes, which we recently explored in a parallel study with an identical experimental design (Salehinejad et al., 2021). The use of measures of different modalities in this study allows us to comprehensively investigate the impact of sleep deprivation on brain and cognitive functions which is largely missing in the human literature."

We added more details about the rationale for saliva sampling:

"We also assessed resting-EEG theta/alpha, as an indirect measure of homeostatic sleep pressure, and examined cortisol and melatonin concentration to see how these are affected under sleep conditions, given the reported mixed effects in previous studies."

We also rephrased the cortical excitability results. Please see the revised text below:

"Taken together, our results demonstrate that glutamate-related intracortical excitability is upscaled after sleep deprivation. Moreover, cortical inhibition was decreased or turned into facilitation, which is indicative of enhanced cortical excitability as a result of GABAergic reduction. Corticospinal excitability did only show a trendwise upscaling, indicative for a major contribution of cortical, but not downstream excitability to this sleep deprivation-related enhancement."

"The increase of cortical excitability parameters and the resultant synaptic saturation following sleep deprivation can explain the respective cognitive performance decline. It is, however, worth noting that our study was not powered to identify these correlations with sufficient reliability, and future studies that are powered for this aim are needed.

Our findings have several implications. First, they show that sleep and circadian preference (i.e., chronotype) have functionally different impacts on human brain physiology and cognition. The same parameters of brain physiology and cognition were recently investigated at circadian optimal vs non-optimal time of day in two groups of early and late chronotypes (Salehinejad et al., 2021). While we found decreased cortical facilitation and lower neuroplasticity induction (same for both LTP and LTD) at the circadian nonpreferred time in that study (Salehinejad et al., 2021), in the present study we observed upscaled cortical excitability and a functionally different pattern of neuroplasticity alteration (i.e., diminished LTP-like plasticity induction and conversion of LTD- to LTP-like plasticity)."

2) EEG-measures. In general, I find the presented evidence regarding a link between synaptic strength and human theta-power is weak. In humans, rhythmic theta activity can be found mostly in the form of midfrontal theta. Here, the largest changes seem to be in posterior electrodes (judging according to in Fig 4 bottom row), which will not capture rhythmic midfrontal theta in humans. Can the authors explain the scaling of the Fig. 4 top vs. bottom row, there seems to be a mismatch? No legend is given for the bottom row. The activity captured here is probably related to changes in nonrhythmic 1/f-type activity (which displays large changes relating to arousal: e.g. https://elifesciences.org/articles/55092. It would be of benefit to see a power spectrum for the EEG-measures to see the specific type of power changes across all frequencies & to verify that these are actually oscillatory peaks in individual subjects. As far as I understood, the referenced study Vyazovskiy et al., 2008 contains no information regarding theta as a marker for synaptic potentiation. The evidence that synaptic strength is captured by the specifically used measures needs to be strengthened or statements like "measured synaptic strength via the resting-EEG theta/alpha pattern" need to be more carefully stated.

Thank you for this comment. We removed the Pz electrode from the figure and instead added F3 and F4 along with Fz and Cz to capture more mid-frontal regions. Please see the revised Figure 4. The top rows now include only midfrontal and midcentral areas (Fz, Cz, F3, F4), and show numerical comparisons of midfrontal theta which is significantly different across conditions (and larger after sleep deprivation). The purpose of the bottom figures, which are removed now, was just to provide an overall visual comparison of theta distribution across sleep conditions. However, we agree that the bottom-row figures are misleading because these just capture average theta band power without specifying midfrontal regions. We removed this part of the figure to prevent confusion. Please see below.

Regarding the power spectrum, we also added new figures (4 g) showing how different frequency bands of the power spectrum are affected by sleep deprivation. Please see the revised Figure 4 below.

Updated results, page 12-13:

"In line with this, we investigated how sleep deprivation affects resting-state brain oscillations at the theta band (4-7 Hz), the beta band (15-30 Hz) as another marker of cortical excitability, vigilance and arousal (Eoh et al., 2005; Fischer et al., 2008) and the alpha band (8-14 Hz) which is important for cognition (e.g. memory, attention) (Klimesch, 2012). To this end, we analyzed EEG spectral power at mid-frontocentral electrodes (Fz, Cz, F3, F4) using a 4×2 mixed ANOVA. For theta activity, significant main effects of location (F1.71=18.68, p<0.001; ηp2=0.40) and sleep condition (F1=17.82, p<0.001; ηp2=0.39), but no interaction was observed, indicating that theta oscillations at frontocentral regions were similarly affected by sleep deprivation. Post hoc tests (paired, p<0.05) revealed that theta oscillations, grand averaged at mid-central electrodes, were significantly increased after sleep deprivation (p<0.001) (Fig. 4a,b). For the alpha band, the main effects of location (F1.49=12.92, p<0.001; ηp2=0.31) and sleep condition (F1=5.03, p=0.033; ηp2=0.15) and their interaction (F2.31=4.60, p=0.010; ηp2=0.14) were significant. Alpha oscillations, grand averaged at mid-frontocentral electrodes, were significantly decreased after sleep deprivation (p=0.033) (Fig. 4c,d). Finally, the analysis of beta spectral power showed significant main effects of location (F1.34=6.73, p=0.008; ηp2=0.19) and sleep condition (F1=6.98, p=0.013; ηp2=0.20) but no significant interaction. Beta oscillations, grand averaged at mid-frontocentral electrodes, were significantly increased after sleep deprivation (p=0.013) (Fig. 4e,f)."

Fig. 4. Resting-state theta, alpha, and beta oscillations at electrodes Fz, Cz, F3 and F4. a,b Theta band activity was significantly higher after the sleep deprivation vs sufficient sleep condition (tFz=4.61, p<0.001; tCz=2.22, p=0.034; tF3=2.93, p=0.007; tF4=4.78, p<0.001). c,d, Alpha band activity was significantly lower at electrodes Fz and Cz (tFz=2.39, p=0.023; tCz=2.65, p=0.013) after the sleep deprivation vs the sufficient sleep condition. e,f, Beta band activity was significantly higher at electrodes Fz, Cz and F4 after sleep deprivation compared with the sufficient sleep condition (tFz=3.06, p=0.005; tCz=2.38, p= 0.024; tF4=2.25, p=0.032). g, Power spectrum including theta (4-7 Hz), alpha (8-14 Hz), and beta (15-30 Hz) bands at the electrodes Fz, Cz, F3 and F4 respectively. Data of one participant were excluded due to excessive noise. All pairwise comparisons for each electrode were calculated via post hoc Student’s t-tests (paired, p<0.05). n=29. Error bars represent s.e.m. ns = nonsignificant; Asterisks indicate significant differences. Boxes indicate the interquartile range that contains 50% of values (range from the 25th to the 75th percentile) and whiskers show the 1 to 99 percentiles.

Regarding the reference, unfortunately, we were referring to a different work of the Vyazovskiy team. We meant Vyazovskiy et al. (2005). We removed this reference and the part that needed to be toned down from the introduction and added new relevant references while tuning down the statement about synaptic strength. Please see below:

Revised text, Results, page 12:

"So far, we found that sleep deprivation upscales cortical excitability, prevents induction of LTP-like plasticity, presumably due to saturated synaptic potentiation, and converts LTD- into LTP-like plasticity. Previous studies in animals (Vyazovskiy and Tobler, 2005; Leemburg et al., 2010) and humans (Finelli et al., 2000) have shown that EEG theta activity is a marker for homeostatic sleep pressure and increased cortical excitability (Kuhn et al., 2016)."

3) In general, the authors generally do a good job pointing out multiple comparison corrected tests. In some cases, e.g. for their correlational analyses across measures, significant results are reported, but without a clearer discussion on what other tests were computed and how correction was applied, the evidence strength of these are hard to evaluate. Please check for all presented correlations.

Thank you for your comment. For correlational analyses, no correction for multiple comparisons was computed, because these were secondary exploratory analyses. We state this now clearly in the manuscript. For the other analyses, the description of multiple comparisons is included below:

Methods, pages 35-37:

"For the TMS protocols with a double-pulse condition (i.e., SICI-ICF, I-wave facilitation, SAI), the resulting mean values were normalized to the respective single-pulse condition. First, mean values were calculated individually and then inter-individual means were calculated for each condition. For the I-O curves, absolute MEP values were used. To test for statistical significance, repeated-measures ANOVAs were performed with ISIs, TMS intensity (in I-O curve only), and condition (sufficient sleep vs sleep deprivation) as within-subject factors and MEP amplitude as the dependent variable. In case of significant results of the ANOVA, post hoc comparisons were performed using Bonferroni-corrected t-tests to compare mean MEP amplitudes of each condition against the baseline MEP and to contrast sufficient sleep vs sleep deprivation conditions. To determine if individual baseline measures differed within and between sessions, SI1mV and Baseline MEP were entered as dependent variables in a mixed-model ANOVA with session (4 levels) and condition (sufficient sleep vs sleep deprivation) as within-subject factors, and group (anodal vs cathodal) as between-subject factor. The mean MEP amplitude for each measurement time-point was normalized to the session’s baseline (individual quotient of the mean from the baseline mean) resulting in values representing either increased (> 1.0) or decreased (< 1.0) excitability. Individual averages of the normalized MEP from each time-point were then calculated and entered as dependent variables in a mixed-model ANOVA with repeated measures with stimulation condition (active, sham), time-point (8 levels), and sleep condition (normal vs deprivation) as within-subject factors and group (anodal vs cathodal) as between-subject factor. In case of significant ANOVA results, post hoc comparisons of MEP amplitudes at each time point were performed using Bonferroni-corrected t-tests to examine if active stimulation resulted in a significant difference relative to sham (comparison 1), baseline (comparison 2), the respective stimulation condition at sufficient sleepvs sleep deprivation (comparison 3), and the between-group comparisons at respective timepoints (comparison 4).

The mean RT, RT variability and accuracy of blocks were entered as dependent variables in repeated-measures ANOVAs with block (5, vs 6, 6 vs 7) and condition (sufficient sleep vs sleep deprivation) as within-subject factors. Because the RT differences between blocks 5 vs 6 and 6 vs 7 were those of major interest, post hoc comparisons were performed on RT differences between these blocks using paired-sample t-tests (two-tailed, p<0.05) without correction for multiple comparisons. For 3-back, Stroop and AX-CPT tasks, mean and standard deviation of RT and accuracy were calculated and entered as dependent variables in repeated-measures ANOVAs with sleep condition (sufficient sleep vs sleep deprivation) as the within-subject factor. For significant ANOVA results, post hoc comparisons of dependent variables were performed using paired-sample t-tests (two-tailed, p<0.05) without correction for multiple comparisons.

For the resting-state data, brain oscillations at mid-central electrodes (Fz, Cz, F3, F4) were analyzed with a 4×2 ANOVA with location (Fz, Cz, F3, F4) and sleep condition (sufficient sleep vs sleep deprivation) as the within-subject factors. For all tasks, individual ERP means were grand-averaged and entered as dependent variables in repeated-measures ANOVAs with sleep condition (sufficient sleep vs sleep deprivation) as the within-subject factor. Post hoc comparisons of grand-averaged amplitudes was performed using paired-sample t-tests (two-tailed, p<0.05) without correction for multiple comparisons.

To assess the relationship between induced neuroplasticity and motor sequence learning, and the relationship between cortical excitability and cognitive task performance, we calculated Pearson correlations. For the first correlation, we used individual grand-averaged MEP amplitudes obtained from anodal and cathodal tDCS pooled for the time-points between 0, and 20 min after interventions, and individual motor learning performance (i.e. BL6-5 and BL6-7 RT difference) across sleep conditions. For the second correlation, we used individual grand-averaged MEP amplitudes obtained from each TMS protocol and individual accuracy/RT obtained from each task across sleep conditions. No correction for multiple comparisons was done for correlational analyses as these were secondary exploratory analyses."

There are also inconsistencies like: " The average levels of cortisol and melatonin were lower after sleep deprivation vs sufficient sleep (cortisol: 3.51{plus minus}2.20 vs 4.85{plus minus}3.23, p=0.05; melatonin 10.50{plus minus}10.66 vs 16.07{plus minus}14.94, p=0.16)"

The p-values are not significant here?

Thank you for your comment. The p-value was only marginally significant for the cortisol level changes. We clarified this in the revision. Please see below:

Revised text, page 19:

"The average levels of cortisol and melatonin were numerically lower after sleep deprivation vs sufficient sleep (cortisol: 3.51±2.20 vs 4.85±3.23, p=0.056; melatonin 10.50±10.66 vs 16.07±14.94, p=0.16), but these differences were only marginally significant for the cortisol level and showed only a trendwise reduction for melatonin."

Reviewer #2:

This study represents the currently most comprehensive characterization of indices of synaptic plasticity and cognition in humans in the context of sleep deprivation. It provides further support for an interplay between the time course of synaptic strength/cortical excitability (homeostatic plasticity) and the inducibility of associative synaptic LTP- LTD-like plasticity. The study is of great interest, the translation of findings is of potential clinical relevance, the methods appear to be solid and the results are mostly convincing. I believe that the writing of the manuscript should be improved (e.g. quality of referencing), clearer framework and hypothesis, reduction of redundancies, and more precise discussion. However, all of these points can be addressed since the overall concept, design, conduct and findings are convincing and of great interest to the field of sleep research, but also more broader to the neurosciences, to clinicians and the public.

We appreciate the reviewer's time for carefully reading our work and providing important suggestions/recommendations.

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 #1 (Public Review):

In this article, Bollmann and colleagues demonstrated both theoretically and experimentally that blood vessels could be targeted at the mesoscopic scale with time-of-flight magnetic resonance imaging (TOF-MRI). With a mathematical model that includes partial voluming effects explicitly, they outline how small voxels reduce the dependency of blood dwell time, a key parameter of the TOF sequence, on blood velocity. Through several experiments on three human subjects, they show that increasing resolution improves contrast and evaluate additional issues such as vessel displacement artifacts and the separation of veins and arteries.

The overall presentation of the main finding, that small voxels are beneficial for mesoscopic pial vessels, is clear and well discussed, although difficult to grasp fully without a good prior understanding of the underlying TOF-MRI sequence principles. Results are convincing, and some of the data both raw and processed have been provided publicly. Visual inspection and comparisons of different scans are provided, although no quantification or statistical comparison of the results are included.

Potential applications of the study are varied, from modeling more precisely functional MRI signals to assessing the health of small vessels. Overall, this article reopens a window on studying the vasculature of the human brain in great detail, for which studies have been surprisingly limited until recently.

In summary, this article provides a clear demonstration that small pial vessels can indeed be imaged successfully with extremely high voxel resolution. There are however several concerns with the current manuscript, hopefully addressable within the study.

Thank you very much for this encouraging review. While smaller voxel sizes theoretically benefit all blood vessels, we are specifically targeting the (small) pial arteries here, as the inflow-effect in veins is unreliable and susceptibility-based contrasts are much more suited for this part of the vasculature. (We have clarified this in the revised manuscript by substituting ‘vessel’ with ‘artery’ wherever appropriate.) Using a partial-volume model and a relative contrast formulation, we find that the blood delivery time is not the limiting factor when imaging pial arteries, but the voxel size is. Taking into account the comparatively fast blood velocities even in pial arteries with diameters ≤ 200 µm (using t_delivery=l_voxel/v_blood), we find that blood dwell times are sufficiently long for the small voxel sizes considered here to employ the simpler formulation of the flow-related enhancement effect. In other words, small voxels eliminate blood dwell time as a consideration for the blood velocities expected for pial arteries.

We have extended the description of the TOF-MRA sequence in the revised manuscript, and all data and simulations/analyses presented in this manuscript are now publicly available at https://osf.io/nr6gc/ and https://gitlab.com/SaskiaB/pialvesseltof.git, respectively. This includes additional quantifications of the FRE effect for large vessels (adding to the assessment for small vessels already included), and the effect of voxel size on vessel segmentations.

Main points:

1) The manuscript needs clarifying through some additional background information for a readership wider than expert MR physicists. The TOF-MRA sequence and its underlying principles should be introduced first thing, even before discussing vascular anatomy, as it is the key to understanding what aspects of blood physiology and MRI parameters matter here. MR physics shorthand terms should be avoided or defined, as 'spins' or 'relaxation' are not obvious to everybody. The relationship between delivery time and slab thickness should be made clear as well.

Thank you for this valuable comment that the Theory section is perhaps not accessible for all readers. We have adapted the manuscript in several locations to provide more background information and details on time-of-flight contrast. We found, however, that there is no concise way to first present the MR physics part and then introduce the pial arterial vasculature, as the optimization presented therein is targeted towards this structure. To address this comment, we have therefore opted to provide a brief introduction to TOF-MRA first in the Introduction, and then a more in-depth description in the Theory section.

Introduction section:

"Recent studies have shown the potential of time-of-flight (TOF) based magnetic resonance angiography (MRA) at 7 Tesla (T) in subcortical areas (Bouvy et al., 2016, 2014; Ladd, 2007; Mattern et al., 2018; Schulz et al., 2016; von Morze et al., 2007). In brief, TOF-MRA uses the high signal intensity caused by inflowing water protons in the blood to generate contrast, rather than an exogenous contrast agent. By adjusting the imaging parameters of a gradient-recalled echo (GRE) sequence, namely the repetition time (T_R) and flip angle, the signal from static tissue in the background can be suppressed, and high image intensities are only present in blood vessels freshly filled with non-saturated inflowing blood. As the blood flows through the vasculature within the imaging volume, its signal intensity slowly decreases. (For a comprehensive introduction to the principles of MRA, see for example Carr and Carroll (2012)). At ultra-high field, the increased signal-to-noise ratio (SNR), the longer T_1 relaxation times of blood and grey matter, and the potential for higher resolution are key benefits (von Morze et al., 2007)."

Theory section:

"Flow-related enhancement

Before discussing the effects of vessel size, we briefly revisit the fundamental theory of the flow-related enhancement effect used in TOF-MRA. Taking into account the specific properties of pial arteries, we will then extend the classical description to this new regime. In general, TOF-MRA creates high signal intensities in arteries using inflowing blood as an endogenous contrast agent. The object magnetization—created through the interaction between the quantum mechanical spins of water protons and the magnetic field—provides the signal source (or magnetization) accessed via excitation with radiofrequency (RF) waves (called RF pulses) and the reception of ‘echo’ signals emitted by the sample around the same frequency. The T1-contrast in TOF-MRA is based on the difference in the steady-state magnetization of static tissue, which is continuously saturated by RF pulses during the imaging, and the increased or enhanced longitudinal magnetization of inflowing blood water spins, which have experienced no or few RF pulses. In other words, in TOF-MRA we see enhancement for blood that flows into the imaging volume."

"Since the coverage or slab thickness in TOF-MRA is usually kept small to minimize blood delivery time by shortening the path-length of the vessel contained within the slab (Parker et al., 1991), and because we are focused here on the pial vasculature, we have limited our considerations to a maximum blood delivery time of 1000 ms, with values of few hundreds of milliseconds being more likely."

2) The main discussion of higher resolution leading to improvements rather than loss presented here seems a bit one-sided: for a more objective understanding of the differences it would be worth to explicitly derive the 'classical' treatment and show how it leads to different conclusions than the present one. In particular, the link made in the discussion between using relative magnetization and modeling partial voluming seems unclear, as both are unrelated. One could also argue that in theory higher resolution imaging is always better, but of course there are practical considerations in play: SNR, dynamics of the measured effect vs speed of acquisition, motion, etc. These issues are not really integrated into the model, even though they provide strong constraints on what can be done. It would be good to at least discuss the constraints that 140 or 160 microns resolution imposes on what is achievable at present.

Thank you for this excellent suggestion. We found it instructive to illustrate the different effects separately, i.e. relative vs. absolute FRE, and then partial volume vs. no-partial volume effects. In response to comment R2.8 of Reviewer 2, we also clarified the derivation of the relative FRE vs the ‘classical’ absolute FRE (please see R2.8). Accordingly, the manuscript now includes the theoretical derivation in the Theory section and an explicit demonstration of how the classical treatment leads to different conclusions in the Supplementary Material. The important insight gained in our work is that only when considering relative FRE and partial-volume effects together, can we conclude that smaller voxels are advantageous. We have added the following section in the Supplementary Material:

"Effect of FRE Definition and Interaction with Partial-Volume Model

For the definition of the FRE effect employed in this study, we used a measure of relative FRE (Al-Kwifi et al., 2002) in combination with a partial-volume model (Eq. 6). To illustrate the implications of these two effects, as well as their interaction, we have estimated the relative and absolute FRE for an artery with a diameter of 200 µm or 2 000 µm (i.e. no partial-volume effects at the centre of the vessel). The absolute FRE expression explicitly takes the voxel volume into account, and so instead of Eq. (6) for the relative FRE we used"

Eq. (1)

"Note that the division by M_zS^tissue⋅l_voxel^3 to obtain the relative FRE from this expression removes the contribution of the total voxel volume (l_voxel^3). Supplementary Figure 2 shows that, when partial volume effects are present, the highest relative FRE arises in voxels with the same size as or smaller than the vessel diameter (Supplementary Figure 2A), whereas the absolute FRE increases with voxel size (Supplementary Figure 2C). If no partial-volume effects are present, the relative FRE becomes independent of voxel size (Supplementary Figure 2B), whereas the absolute FRE increases with voxel size (Supplementary Figure 2D). While the partial-volume effects for the relative FRE are substantial, they are much more subtle when using the absolute FRE and do not alter the overall characteristics."

Supplementary Figure 2: Effect of voxel size and blood delivery time on the relative flow-related enhancement (FRE) using either a relative (A,B) (Eq. (3)) or an absolute (C,D) (Eq. (12)) FRE definition assuming a pial artery diameter of 200 μm (A,C) or 2 000 µm, i.e. no partial-volume effects at the central voxel of this artery considered here.

In addition, we have also clarified the contribution of the two definitions and their interaction in the Discussion section. Following the suggestion of Reviewer 2, we have extended our interpretation of relative FRE. In brief, absolute FRE is closely related to the physical origin of the contrast, whereas relative FRE is much more concerned with the “segmentability” of a vessel (please see R2.8 for more details):

"Extending classical FRE treatments to the pial vasculature

There are several major modifications in our approach to this topic that might explain why, in contrast to predictions from classical FRE treatments, it is indeed possible to image pial arteries. For instance, the definition of vessel contrast or flow-related enhancement is often stated as an absolute difference between blood and tissue signal (Brown et al., 2014a; Carr and Carroll, 2012; Du et al., 1993, 1996; Haacke et al., 1990; Venkatesan and Haacke, 1997). Here, however, we follow the approach of Al-Kwifi et al. (2002) and consider relative contrast. While this distinction may seem to be semantic, the effect of voxel volume on FRE for these two definitions is exactly opposite: Du et al. (1996) concluded that larger voxel size increases the (absolute) vessel-background contrast, whereas here we predict an increase in relative FRE for small arteries with decreasing voxel size. Therefore, predictions of the depiction of small arteries with decreasing voxel size differ depending on whether one is considering absolute contrast, i.e. difference in longitudinal magnetization, or relative contrast, i.e. contrast differences independent of total voxel size. Importantly, this prediction changes for large arteries where the voxel contains only vessel lumen, in which case the relative FRE remains constant across voxel sizes, but the absolute FRE increases with voxel size (Supplementary Figure 2). Overall, the interpretations of relative and absolute FRE differ, and one measure may be more appropriate for certain applications than the other. Absolute FRE describes the difference in magnetization and is thus tightly linked to the underlying physical mechanism. Relative FRE, however, describes the image contrast and segmentability. If blood and tissue magnetization are equal, both contrast measures would equal zero and indicate that no contrast difference is present. However, when there is signal in the vessel and as the tissue magnetization approaches zero, the absolute FRE approaches the blood magnetization (assuming no partial-volume effects), whereas the relative FRE approaches infinity. While this infinite relative FRE does not directly relate to the underlying physical process of ‘infinite’ signal enhancement through inflowing blood, it instead characterizes the segmentability of the image in that an image with zero intensity in the background and non-zero values in the structures of interest can be segmented perfectly and trivially. Accordingly, numerous empirical observations (Al-Kwifi et al., 2002; Bouvy et al., 2014; Haacke et al., 1990; Ladd, 2007; Mattern et al., 2018; von Morze et al., 2007) and the data provided here (Figure 5, 6 and 7) have shown the benefit of smaller voxel sizes if the aim is to visualize and segment small arteries."

Note that our formulation of the FRE—even without considering SNR—does not suggest that higher resolution is always better, but instead should be matched to the size of the target arteries:

"Importantly, note that our treatment of the FRE does not suggest that an arbitrarily small voxel size is needed, but instead that voxel sizes appropriate for the arterial diameter of interest are beneficial (in line with the classic “matched-filter” rationale (North, 1963)). Voxels smaller than the arterial diameter would not yield substantial benefits (Figure 5) and may result in SNR reductions that would hinder segmentation performance."

Further, we have also extended the concluding paragraph of the Imaging limitation section to also include a practical perspective:

"In summary, numerous theoretical and practical considerations remain for optimal imaging of pial arteries using time-of-flight contrast. Depending on the application, advanced displacement artefact compensation strategies may be required, and zero-filling could provide better vessel depiction. Further, an optimal trade-off between SNR, voxel size and acquisition time needs to be found. Currently, the partial-volume FRE model only considers voxel size, and—as we reduced the voxel size in the experiments—we (partially) compensated the reduction in SNR through longer scan times. This, ultimately, also required the use of prospective motion correction to enable the very long acquisition times necessary for 140 µm isotropic voxel size. Often, anisotropic voxels are used to reduce acquisition time and increase SNR while maintaining in-plane resolution. This may indeed prove advantageous when the (also highly anisotropic) arteries align with the anisotropic acquisition, e.g. when imaging the large supplying arteries oriented mostly in the head-foot direction. In the case of pial arteries, however, there is not preferred orientation because of the convoluted nature of the pial arterial vasculature encapsulating the complex folding of the cortex (see section Anatomical architecture of the pial arterial vasculature). A further reduction in voxel size may be possible in dedicated research settings utilizing even longer acquisition times and/or larger acquisition volumes to maintain SNR. However, if acquisition time is limited, voxel size and SNR need to be carefully balanced against each other."

3) The article seems to imply that TOF-MRA is the only adequate technique to image brain vasculature, while T2 mapping, UHF T1 mapping (see e.g. Choi et al., https://doi.org/10.1016/j.neuroimage.2020.117259) phase (e.g. Fan et al., doi:10.1038/jcbfm.2014.187), QSM (see e.g. Huck et al., https://doi.org/10.1007/s00429-019-01919-4), or a combination (Bernier et al., https://doi.org/10.1002/hbm.24337​, Ward et al., https://doi.org/10.1016/j.neuroimage.2017.10.049) all depict some level of vascular detail. It would be worth quickly reviewing the different effects of blood on MRI contrast and how those have been used in different approaches to measure vasculature. This would in particular help clarify the experiment combining TOF with T2 mapping used to separate arteries from veins (more on this question below).

We apologize if we inadvertently created the impression that TOF-MRA is a suitable technique to image the complete brain vasculature, and we agree that susceptibility-based methods are much more suitable for venous structures. As outlined above, we have revised the manuscript in various sections to indicate that it is the pial arterial vasculature we are targeting. We have added a statement on imaging the venous vasculature in the Discussion section. Please see our response below regarding the use of T2* to separate arteries and veins.

"The advantages of imaging the pial arterial vasculature using TOF-MRA without an exogenous contrast agent lie in its non-invasiveness and the potential to combine these data with various other structural and functional image contrasts provided by MRI. One common application is to acquire a velocity-encoded contrast such as phase-contrast MRA (Arts et al., 2021; Bouvy et al., 2016). Another interesting approach utilises the inherent time-of-flight contrast in magnetization-prepared two rapid acquisition gradient echo (MP2RAGE) images acquired at ultra-high field that simultaneously acquires vasculature and structural data, albeit at lower achievable resolution and lower FRE compared to the TOF-MRA data in our study (Choi et al., 2020). In summary, we expect high-resolution TOF-MRA to be applicable also for group studies to address numerous questions regarding the relationship of arterial topology and morphometry to the anatomical and functional organization of the brain, and the influence of arterial topology and morphometry on brain hemodynamics in humans. In addition, imaging of the pial venous vasculature—using susceptibility-based contrasts such as T2-weighted magnitude (Gulban et al., 2021) or phase imaging (Fan et al., 2015), susceptibility-weighted imaging (SWI) (Eckstein et al., 2021; Reichenbach et al., 1997) or quantitative susceptibility mapping (QSM) (Bernier et al., 2018; Huck et al., 2019; Mattern et al., 2019; Ward et al., 2018)—would enable a comprehensive assessment of the complete cortical vasculature and how both arteries and veins shape brain hemodynamics.*"

4) The results, while very impressive, are mostly qualitative. This seems a missed opportunity to strengthen the points of the paper: given the segmentations already made, the amount/density of detected vessels could be compared across scans for the data of Fig. 5 and 7. The minimum distance between vessels could be measured in Fig. 8 to show a 2D distribution and/or a spatial map of the displacement. The number of vessels labeled as veins instead of arteries in Fig. 9 could be given.

We fully agree that estimating these quantitative measures would be very interesting; however, this would require the development of a comprehensive analysis framework, which would considerably shift the focus of this paper from data acquisition and flow-related enhancement to data analysis. As noted in the discussion section Challenges for vessel segmentation algorithms, ‘The vessel segmentations presented here were performed to illustrate the sensitivity of the image acquisition to small pial arteries’, because the smallest arteries tend to be concealed in the maximum intensity projections. Further, the interpretation of these measures is not straightforward. For example, the number of detected vessels for the artery depicted in Figure 5 does not change across resolutions, but their length does. We have therefore estimated the relative increase in skeleton length across resolutions for Figures 5 and 7. However, these estimates are not only a function of the voxel size but also of the underlying vasculature, i.e. the number of arteries with a certain diameter present, and may thus not generalise well to enable quantitative predictions of the improvement expected from increased resolutions. We have added an illustration of these analyses in the Supplementary Material, and the following additions in the Methods, Results and Discussion sections.

"For vessel segmentation, a semi-automatic segmentation pipeline was implemented in Matlab R2020a (The MathWorks, Natick, MA) using the UniQC toolbox (Frässle et al., 2021): First, a brain mask was created through thresholding which was then manually corrected in ITK-SNAP (http://www.itksnap.org/) (Yushkevich et al., 2006) such that pial vessels were included. For the high-resolution TOF data (Figures 6 and 7, Supplementary Figure 4), denoising to remove high frequency noise was performed using the implementation of an adaptive non-local means denoising algorithm (Manjón et al., 2010) provided in DenoiseImage within the ANTs toolbox, with the search radius for the denoising set to 5 voxels and noise type set to Rician. Next, the brain mask was applied to the bias corrected and denoised data (if applicable). Then, a vessel mask was created based on a manually defined threshold, and clusters with less than 10 or 5 voxels for the high- and low-resolution acquisitions, respectively, were removed from the vessel mask. Finally, an iterative region-growing procedure starting at each voxel of the initial vessel mask was applied that successively included additional voxels into the vessel mask if they were connected to a voxel which was already included and above a manually defined threshold (which was slightly lower than the previous threshold). Both thresholds were applied globally but manually adjusted for each slab. No correction for motion between slabs was applied. The Matlab code describing the segmentation algorithm as well as the analysis of the two-echo TOF acquisition outlined in the following paragraph are also included in our github repository (https://gitlab.com/SaskiaB/pialvesseltof.git). To assess the data quality, maximum intensity projections (MIPs) were created and the outline of the segmentation MIPs were added as an overlay. To estimate the increased detection of vessels with higher resolutions, we computed the relative increase in the length of the segmented vessels for the data presented in Figure 5 (0.8 mm, 0.5 mm, 0.4 mm and 0.3 mm isotropic voxel size) and Figure 7 (0.16 mm and 0.14 mm isotropic voxel size) by computing the skeleton using the bwskel Matlab function and then calculating the skeleton length as the number of voxels in the skeleton multiplied by the voxel size."

"To investigate the effect of voxel size on vessel FRE, we acquired data at four different voxel sizes ranging from 0.8 mm to 0.3 mm isotropic resolution, adjusting only the encoding matrix, with imaging parameters being otherwise identical (FOV, TR, TE, flip angle, R, slab thickness, see section Data acquisition). The total acquisition time increases from less than 2 minutes for the lowest resolution scan to over 6 minutes for the highest resolution scan as a result. Figure 5 shows thin maximum intensity projections of a small vessel. While the vessel is not detectable at the largest voxel size, it slowly emerges as the voxel size decreases and approaches the vessel size. Presumably, this is driven by the considerable increase in FRE as seen in the single slice view (Figure 5, small inserts). Accordingly, the FRE computed from the vessel mask for the smallest part of the vessel (Figure 5, red mask) increases substantially with decreasing voxel size. More precisely, reducing the voxel size from 0.8 mm, 0.5 mm or 0.4 mm to 0.3 mm increases the FRE by 2900 %, 165 % and 85 %, respectively. Assuming a vessel diameter of 300 μm, the partial-volume FRE model (section Introducing a partial-volume model) would predict similar ratios of 611%, 178% and 78%. However, as long as the vessel is larger than the voxel (Figure 5, blue mask), the relative FRE does not change with resolution (see also Effect of FRE Definition and Interaction with Partial-Volume Model in the Supplementary Material). To illustrate the gain in sensitivity to detect smaller arteries, we have estimated the relative increase of the total length of the segmented vasculature (Supplementary Figure 9): reducing the voxel size from 0.8 mm to 0.5 mm isotropic increases the skeleton length by 44 %, reducing the voxel size from 0.5 mm to 0.4 mm isotropic increases the skeleton length by 28 %, and reducing the voxel size from 0.4 mm to 0.3 mm isotropic increases the skeleton length by 31 %. In summary, when imaging small pial arteries, these data support the hypothesis that it is primarily the voxel size, not the blood delivery time, which determines whether vessels can be resolved."

"Indeed, the reduction in voxel volume by 33 % revealed additional small branches connected to larger arteries (see also Supplementary Figure 8). For this example, we found an overall increase in skeleton length of 14 % (see also Supplementary Figure 9)."

"We therefore expect this strategy to enable an efficient image acquisition without the need for additional venous suppression RF pulses. Once these challenges for vessel segmentation algorithms are addressed, a thorough quantification of the arterial vasculature can be performed. For example, the skeletonization procedure used to estimate the increase of the total length of the segmented vasculature (Supplementary Figure 9) exhibits errors particularly in the unwanted sinuses and large veins. While they are consistently present across voxel sizes, and thus may have less impact on relative change in skeleton length, they need to be addressed when estimating the absolute length of the vasculature, or other higher-order features such as number of new branches. (Note that we have also performed the skeletonization procedure on the maximum intensity projections to reduce the number of artefacts and obtained comparable results: reducing the voxel size from 0.8 mm to 0.5 mm isotropic increases the skeleton length by 44 % (3D) vs 37 % (2D), reducing the voxel size from 0.5 mm to 0.4 mm isotropic increases the skeleton length by 28 % (3D) vs 26 % (2D), reducing the voxel size from 0.4 mm to 0.3 mm isotropic increases the skeleton length by 31 % (3D) vs 16 % (2D), and reducing the voxel size from 0.16 mm to 0.14 mm isotropic increases the skeleton length by 14 % (3D) vs 24 % (2D).)"

Supplementary Figure 9: Increase of vessel skeleton length with voxel size reduction. Axial maximum intensity projections for data acquired with different voxel sizes ranging from 0.8 mm to 0.3 mm (TOP) (corresponding to Figure 5) and 0.16 mm to 0.14 mm isotropic (corresponding to Figure 7) are shown. Vessel skeletons derived from segmentations performed for each resolution are overlaid in red. A reduction in voxel size is accompanied by a corresponding increase in vessel skeleton length.

Regarding further quantification of the vessel displacement presented in Figure 8, we have estimated the displacement using the Horn-Schunck optical flow estimator (Horn and Schunck, 1981; Mustafa, 2016) (https://github.com/Mustafa3946/Horn-Schunck-3D-Optical-Flow). However, the results are dominated by the larger arteries, whereas we are mostly interested in the displacement of the smallest arteries, therefore this quantification may not be helpful.

Because the theoretical relationship between vessel displacement and blood velocity is well known (Eq. 7), and we have also outlined the expected blood velocity as a function of arterial diameter in Figure 2, which provided estimates of displacements that matched what was found in our data (as reported in our original submission), we believe that the new quantification in this form does not add value to the manuscript. What would be interesting would be to explore the use of this displacement artefact as a measure of blood velocities. This, however, would require more substantial analyses in particular for estimation of the arterial diameter and additional validation data (e.g. phase-contrast MRA). We have outlined this avenue in the Discussion section. What is relevant to the main aim of this study, namely imaging of small pial arteries, is the insight that blood velocities are indeed sufficiently fast to cause displacement artefacts even in smaller arteries. We have clarified this in the Results section:

"Note that correction techniques exist to remove displaced vessels from the image (Gulban et al., 2021), but they cannot revert the vessels to their original location. Alternatively, this artefact could also potentially be utilised as a rough measure of blood velocity."

"At a delay time of 10 ms between phase encoding and echo time, the observed displacement of approximately 2 mm in some of the larger vessels would correspond to a blood velocity of 200 mm/s, which is well within the expected range (Figure 2). For the smallest arteries, a displacement of one voxel (0.4 mm) can be observed, indicative of blood velocities of 40 mm/s. Note that the vessel displacement can be observed in all vessels visible at this resolution, indicating high blood velocities throughout much of the pial arterial vasculature. Thus, assuming a blood velocity of 40 mm/s (Figure 2) and a delay time of 5 ms for the high-resolution acquisitions (Figure 6), vessel displacements of 0.2 mm are possible, representing a shift of 1–2 voxels."

Regarding the number of vessels labelled as veins, please see our response below to R1.5.

In the main quantification given, the estimation of FRE increase with resolution, it would make more sense to perform the segmentation independently for each scan and estimate the corresponding FRE: using the mask from the highest resolution scan only biases the results. It is unclear also if the background tissue measurement one voxel outside took partial voluming into account (by leaving a one voxel free interface between vessel and background). In this analysis, it would also be interesting to estimate SNR, so you can compare SNR and FRE across resolutions, also helpful for the discussion on SNR.

The FRE serves as an indicator of the potential performance of any segmentation algorithm (including manual segmentation) (also see our discussion on the interpretation of FRE in our response to R1.2). If we were to segment each scan individually, we would, in the ideal case, always obtain the same FRE estimate, as FRE influences the performance of the segmentation algorithm. In practice, this simply means that it is not possible to segment the vessel in the low-resolution image to its full extent that is visible in the high-resolution image, because the FRE is too low for small vessels. However, we agree with the core point that the reviewer is making, and so to help address this, a valuable addition would be to compare the FRE for the section of a vessel that is visible at all resolutions, where we found—within the accuracy of the transformations and resampling across such vastly different resolutions—that the FRE does not increase any further with higher resolution if the vessel is larger than the voxel size (page 18 and Figure 5). As stated in the Methods section, and as noted by the reviewer, we used the voxels immediately next to the vessel mask to define the background tissue signal level. Any resulting potential partial-volume effects in these background voxels would affect all voxel sizes, introducing a consistent bias that would not impact our comparison. However, inspection of the image data in Figure 5 showed partial-volume effects predominantly within those voxels intersecting the vessel, rather than voxels surrounding the vessel, in agreement with our model of FRE.

"All imaging data were slab-wise bias-field corrected using the N4BiasFieldCorrection (Tustison et al., 2010) tool in ANTs (Avants et al., 2009) with the default parameters. To compare the empirical FRE across the four different resolutions (Figure 5), manual masks were first created for the smallest part of the vessel in the image with the highest resolution and for the largest part of the vessel in the image with the lowest resolution. Then, rigid-body transformation parameters from the low-resolution to the high-resolution (and the high-resolution to the low-resolution) images were estimated using coregister in SPM (https://www.fil.ion.ucl.ac.uk/spm/), and their inverse was applied to the vessel mask using SPM’s reslice. To calculate the empirical FRE (Eq. (3)), the mean of the intensity values within the vessel mask was used to approximate the blood magnetization, and the mean of the intensity values one voxel outside of the vessel mask was used as the tissue magnetization."

"To investigate the effect of voxel size on vessel FRE, we acquired data at four different voxel sizes ranging from 0.8 mm to 0.3 mm isotropic resolution, adjusting only the encoding matrix, with imaging parameters being otherwise identical (FOV, TR, TE, flip angle, R, slab thickness, see section Data acquisition). The total acquisition time increases from less than 2 minutes for the lowest resolution scan to over 6 minutes for the highest resolution scan as a result. Figure 5 shows thin maximum intensity projections of a small vessel. While the vessel is not detectable at the largest voxel size, it slowly emerges as the voxel size decreases and approaches the vessel size. Presumably, this is driven by the considerable increase in FRE as seen in the single slice view (Figure 5, small inserts). Accordingly, the FRE computed from the vessel mask for the smallest part of the vessel (Figure 5, red mask) increases substantially with decreasing voxel size. More precisely, reducing the voxel size from 0.8 mm, 0.5 mm or 0.4 mm to 0.3 mm increases the FRE by 2900 %, 165 % and 85 %, respectively. Assuming a vessel diameter of 300 μm, the partial-volume FRE model (section Introducing a partial-volume model) would predict similar ratios of 611%, 178% and 78%. However, if the vessel is larger than the voxel (Figure 5, blue mask), the relative FRE remains constant across resolutions (see also Effect of FRE Definition and Interaction with Partial-Volume Model in the Supplementary Material). To illustrate the gain in sensitivity to smaller arteries, we have estimated the relative increase of the total length of the segmented vasculature (Supplementary Figure 9): reducing the voxel size from 0.8 mm to 0.5 mm isotropic increases the skeleton length by 44 %, reducing the voxel size from 0.5 mm to 0.4 mm isotropic increases the skeleton length by 28 %, and reducing the voxel size from 0.4 mm to 0.3 mm isotropic increases the skeleton length by 31 %. In summary, when imaging small pial arteries, these data support the hypothesis that it is primarily the voxel size, not blood delivery time, which determines whether vessels can be resolved."

Figure 5: Effect of voxel size on flow-related vessel enhancement. Thin axial maximum intensity projections containing a small artery acquired with different voxel sizes ranging from 0.8 mm to 0.3 mm isotropic are shown. The FRE is estimated using the mean intensity value within the vessel masks depicted on the left, and the mean intensity values of the surrounding tissue. The small insert shows a section of the artery as it lies within a single slice. A reduction in voxel size is accompanied by a corresponding increase in FRE (red mask), whereas no further increase is obtained once the voxel size is equal or smaller than the vessel size (blue mask).

After many internal discussions, we had to conclude that deducing a meaningful SNR analysis that would benefit the reader was not possible given the available data due to the complex relationship between voxel size and other imaging parameters in practice. In detail, we have reduced the voxel size but at the same time increased the acquisition time by increasing the number of encoding steps—which we have now also highlighted in the manuscript. We have, however, added additional considerations about balancing SNR and segmentation performance. Note that these considerations are not specific to imaging the pial arteries but apply to all MRA acquisitions, and have thus been discussed previously in the literature. Here, we wanted to focus on the novel insights gained in our study. Importantly, while we previously noted that reducing voxel size improves contrast in vessels whose diameters are smaller than the voxel size, we now explicitly acknowledge that, for vessels whose diameters are larger than the voxel size reducing the voxel size is not helpful---since it only reduces SNR without any gain in contrast---and may hinder segmentation performance, and thus become counterproductive.

"In general, we have not considered SNR, but only FRE, i.e. the (relative) image contrast, assuming that segmentation algorithms would benefit from higher contrast for smaller arteries. Importantly, the acquisition parameters available to maximize FRE are limited, namely repetition time, flip angle and voxel size. SNR, however, can be improved via numerous avenues independent of these parameters (Brown et al., 2014b; Du et al., 1996; Heverhagen et al., 2008; Parker et al., 1991; Triantafyllou et al., 2011; Venkatesan and Haacke, 1997), the simplest being longer acquisition times. If the aim is to optimize a segmentation outcome for a given acquisition time, the trade-off between contrast and SNR for the specific segmentation algorithm needs to be determined (Klepaczko et al., 2016; Lesage et al., 2009; Moccia et al., 2018; Phellan and Forkert, 2017). Our own—albeit limited—experience has shown that segmentation algorithms (including manual segmentation) can accommodate a perhaps surprising amount of noise using prior knowledge and neighborhood information, making these high-resolution acquisitions possible. Importantly, note that our treatment of the FRE does not suggest that an arbitrarily small voxel size is needed, but instead that voxel sizes appropriate for the arterial diameter of interest are beneficial (in line with the classic “matched-filter” rationale (North, 1963)). Voxels smaller than the arterial diameter would not yield substantial benefits (Figure 5) and may result in SNR reductions that would hinder segmentation performance."

5) The separation of arterial and venous components is a bit puzzling, partly because the methodology used is not fully explained, but also partly because the reasons invoked (flow artefact in large pial veins) do not match the results (many small vessels are included as veins). This question of separating both types of vessels is quite important for applications, so the whole procedure should be explained in detail. The use of short T2 seemed also sub-optimal, as both arteries and veins result in shorter T2 compared to most brain tissues: wouldn't a susceptibility-based measure (SWI or better QSM) provide a better separation? Finally, since the T2* map and the regular TOF map are at different resolutions, masking out the vessels labeled as veins will likely result in the smaller veins being left out.

We agree that while the technical details of this approach were provided in the Data analysis section, the rationale behind it was only briefly mentioned. We have therefore included an additional section Inflow-artefacts in sinuses and pial veins in the Theory section of the manuscript. We have also extended the discussion of the advantages and disadvantages of the different susceptibility-based contrasts, namely T2, SWI and QSM. While in theory both T2 and QSM should allow the reliable differentiation of arterial and venous blood, we found T2* to perform more robustly, as QSM can fail in many places, e.g., due to the strong susceptibility sources within superior sagittal and transversal sinuses and pial veins and their proximity to the brain surface, dedicated processing is required (Stewart et al., 2022). Further, we have also elaborated in the Discussion section why the interpretation of Figure 9 regarding the absence or presence of small veins is challenging. Namely, the intensity-based segmentation used here provides only an incomplete segmentation even of the larger sinuses, because the overall lower intensity found in veins combined with the heterogeneity of the intensities in veins violates the assumptions made by most vascular segmentation approaches of homogenous, high image intensities within vessels, which are satisfied in arteries (page 29f) (see also the illustration below). Accordingly, quantifying the number of vessels labelled as veins (R1.4a) would provide misleading results, as often only small subsets of the same sinus or vein are segmented.

"Inflow-artefacts in sinuses and pial veins

Inflow in large pial veins and the sagittal and transverse sinuses can cause flow-related enhancement in these non-arterial vessels. One common strategy to remove this unwanted signal enhancement is to apply venous suppression pulses during the data acquisition, which saturate bloods spins outside the imaging slab. Disadvantages of this technique are the technical challenges of applying these pulses at ultra-high field due to constraints of the specific absorption rate (SAR) and the necessary increase in acquisition time (Conolly et al., 1988; Heverhagen et al., 2008; Johst et al., 2012; Maderwald et al., 2008; Schmitter et al., 2012; Zhang et al., 2015). In addition, optimal positioning of the saturation slab in the case of pial arteries requires further investigation, and in particular supressing signal from the superior sagittal sinus without interfering in the imaging of the pial arteries vasculature at the top of the cortex might prove challenging. Furthermore, this venous saturation strategy is based on the assumption that arterial blood is traveling head-wards while venous blood is drained foot-wards. For the complex and convoluted trajectory of pial vessels this directionality-based saturation might be oversimplified, particularly when considering the higher-order branches of the pial arteries and veins on the cortical surface. Inspired by techniques to simultaneously acquire a TOF image for angiography and a susceptibility-weighted image for venography (Bae et al., 2010; Deistung et al., 2009; Du et al., 1994; Du and Jin, 2008), we set out to explore the possibility of removing unwanted venous structures from the segmentation of the pial arterial vasculature during data postprocessing. Because arteries filled with oxygenated blood have T2-values similar to tissue, while veins have much shorter T2-values due to the presence of deoxygenated blood (Pauling and Coryell, 1936; Peters et al., 2007; Uludağ et al., 2009; Zhao et al., 2007), we used this criterion to remove vessels with short T2* values from the segmentation (see Data Analysis for details). In addition, we also explored whether unwanted venous structures in the high-resolution TOF images—where a two-echo acquisition is not feasible due to the longer readout—can be removed based on detecting them in a lower-resolution image."

"Removal of pial veins

Inflow in large pial veins and the superior sagittal and transverse sinuses can cause a flow-related enhancement in these non-arterial vessels (Figure 9, left). The higher concentration of deoxygenated haemoglobin in these vessels leads to shorter T2 values (Pauling and Coryell, 1936), which can be estimated using a two-echo TOF acquisition (see also Inflow-artefacts in sinuses and pial veins). These vessels can be identified in the segmentation based on their T2 values (Figure 9, left), and removed from the angiogram (Figure 9, right) (Bae et al., 2010; Deistung et al., 2009; Du et al., 1994; Du and Jin, 2008). In particular, the superior and inferior sagittal and the transversal sinuses and large veins which exhibited an inhomogeneous intensity profile and a steep loss of intensity at the slab boundary were identified as non-arterial (Figure 9, left). Further, we also explored the option of removing unwanted venous vessels from the high-resolution TOF image (Figure 7) using a low-resolution two-echo TOF (not shown). This indeed allowed us to remove the strong signal enhancement in the sagittal sinuses and numerous larger veins, although some small veins, which are characterised by inhomogeneous intensity profiles and can be detected visually by experienced raters, remain."

Figure 9: Removal of non-arterial vessels in time-of-flight imaging. LEFT: Segmentation of arteries (red) and veins (blue) using T_2^ estimates. RIGHT: Time-of-flight angiogram after vein removal.*

Our approach also assumes that the unwanted veins are large enough that they are also resolved in the low-resolution image. If we consider the source of the FRE effect, it might indeed be exclusively large veins that are present in TOF-MRA data, which would suggest that our assumption is valid. Fundamentally, the FRE depends on the inflow of un-saturated spins into the imaging slab. However, small veins drain capillary beds in the local tissue, i.e. the tissue within the slab. (Note that due to the slice oversampling implemented in our acquisition, spins just above or below the slab will also be excited.) Thus, small veins only contain blood water spins that have experienced a large number of RF pulses due to the long transit time through the pial arterial vasculature, the capillaries and the intracortical venules. Hence, their longitudinal magnetization would be similar to that of stationary tissue. To generate an FRE effect in veins, “pass-through” venous blood from outside the imaging slab is required. This is only available in veins that are passing through the imaging slab, which have much larger diameters. These theoretical considerations are corroborated by the findings in Figure 9, where large disconnected vessels with varying intensity profiles were identified as non-arterial. Due to the heterogenous intensity profiles in large veins and the sagittal and transversal sinuses, the intensity-based segmentation applied here may only label a subset of the vessel lumen, creating the impression of many small veins. This is particularly the case for the straight and inferior sagittal sinus in the bottom slab of Figure 9. Nevertheless, future studies potentially combing anatomical prior knowledge, advanced segmentation algorithms and susceptibility measures would be capable of removing these unwanted veins in post-processing to enable an efficient TOF-MRA image acquisition dedicated to optimally detecting small arteries without the need for additional venous suppression RF pulses.

6) A more general question also is why this imaging method is limited to pial vessels: at 140 microns, the larger intra-cortical vessels should be appearing (group 6 in Duvernoy, 1981: diameters between 50 and 240 microns). Are there other reasons these vessels are not detected? Similarly, it seems there is no arterial vasculature detected in the white matter here: it is due to the rather superior location of the imaging slab, or a limitation of the method? Likewise, all three results focus on a rather homogeneous region of cerebral cortex, in terms of vascularisation. It would be interesting for applications to demonstrate the capabilities of the method in more complex regions, e.g. the densely vascularised cerebellum, or more heterogeneous regions like the midbrain. Finally, it is notable that all three subjects appear to have rather different densities of vessels, from sparse (participant II) to dense (participant I), with some inhomogeneities in density (frontal region in participant III) and inconsistencies in detection (sinuses absent in participant II). All these points should be discussed.

While we are aware that the diameter of intracortical arteries has been suggested to be up to 240 µm (Duvernoy et al., 1981), it remains unclear how prevalent intracortical arteries of this size are. For example, note that in a different context in the Duvernoy study (in teh revised manuscript), the following values are mentioned (which we followed in Figure 1):

“Central arteries of the Iobule always have a large diameter of 260 µ to 280 µ, at their origin. Peripheral arteries have an average diameter of 150 µ to 180 µ. At the cortex surface, all arterioles of 50 µ or less, penetrate the cortex or form anastomoses. The diameter of most of these penetrating arteries is approximately 40 µ.”

Further, the examinations by Hirsch et al. (2012) (albeit in the macaque brain), showed one (exemplary) intracortical artery belonging to group 6 (Figure 1B), whose diameter appears to be below 100 µm. Given these discrepancies and the fact that intracortical arteries in group 5 only reach 75 µm, we suspect that intracortical arteries with diameters > 140 µm are a very rare occurrence, which we might not have encountered in this data set.

Similarly, arteries in white matter (Nonaka et al., 2003) and the cerebellum (Duvernoy et al., 1983) are beyond our resolution at the moment. The midbrain is an interesting suggesting, although we believe that the cortical areas chosen here with their gradual reduction in diameter along the vascular tree, provide a better illustration of the effect of voxel size than the rather abrupt reduction in vascular diameter found in the midbrain. We have added the even higher resolution requirements in the discussion section:

"In summary, we expect high-resolution TOF-MRA to be applicable also for group studies, to address numerous questions regarding the relationship of arterial topology and morphometry to the anatomical and functional organization of the brain, and the influence of arterial topology and morphometry on brain hemodynamics in humans. Notably, we have focused on imaging pial arteries of the human cerebrum; however, other brain structures such as the cerebellum, subcortex and white matter are of course also of interest. While the same theoretical considerations apply, imaging the arterial vasculature in these structures will require even smaller voxel sizes due to their smaller arterial diameters (Duvernoy et al., 1983, 1981; Nonaka et al., 2003)."

Regarding the apparent sparsity of results from participant II, this is mostly driven by the much smaller coverage in this subject (19.6 mm in Participant II vs. 50 mm and 58 mm in Participant I and III, respectively). The reduction in density in the frontal regions might indeed constitute difference in anatomy or might be driven by the presence or more false-positive veins in Participant I than Participant III in these areas. Following the depiction in Duvernoy et al. (1981), one would not expect large arteries in frontal areas, but large veins are common. Thus, the additional vessels in Participant I in the frontal areas might well be false-positive veins, and their removal would result in similar densities for both participants. Indeed, as pointed out in section Future directions, we would expect a lower arterial density in frontal and posterior areas than in middle areas. The sinuses (and other large false-positive veins) in Participant II have been removed as outlined and discussed in sections Removal of pial veins and Challenges for vessel segmentation algorithms, respectively.

7) One of the main practical limitations of the proposed method is the use of a very small imaging slab. It is mentioned in the discussion that thicker slabs are not only possible, but beneficial both in terms of SNR and acceleration possibilities. What are the limitations that prevented their use in the present study? With the current approach, what would be the estimated time needed to acquire the vascular map of an entire brain? It would also be good to indicate whether specific processing was needed to stitch together the multiple slab images in Fig. 6-9, S2.

Time-of-flight acquisitions are commonly performed with thin acquisition slabs, following initial investigations by Parker et al. (1991) to maximise vessel sensitivity and minimize noise. We therefore followed this practice for our initial investigations but wanted to point out in the discussion that thicker slabs might provide several advantages that need to be evaluated in future studies. This would include theoretical and empirical evaluations balancing SNR gains from larger excitation volumes and SNR losses due to more acceleration. For this study, we have chosen the slab thickness such as to keep the acquisition time at a reasonable amount to minimize motion artefacts (as outlined in the Discussion). In addition, due to the extreme matrix sizes in particular for the 0.14 mm acquisition, we were also limited in the number of data points per image that can be indexed. This would require even more substantial changes to the sequence than what we have already performed. With 16 slabs, assuming optimal FOV orientation, full-brain coverage including the cerebellum of 95 % of the population (Mennes et al., 2014) could be achieved with an acquisition time of (16  11 min 42 s = 3 h 7 min 12 s) at 0.16 mm isotropic voxel size. No stitching of the individual slabs was performed, as subject motion was minimal. We have added a corresponding comment in the Data Analysis.

"Both thresholds were applied globally but manually adjusted for each slab. No correction for motion between slabs was applied as subject motion was minimal. The Matlab code describing the segmentation algorithm as well es the analysis of the two-echo TOF acquisition outlined in the following paragraph are also included in the github repository (https://gitlab.com/SaskiaB/pialvesseltof.git)."

8) Some researchers and clinicians will argue that you can attain best results with anisotropic voxels, combining higher SNR and higher resolution. It would be good to briefly mention why isotropic voxels are preferred here, and whether anisotropic voxels would make sense at all in this context.

Anisotropic voxels can be advantageous if the underlying object is anisotropic, e.g. an artery running straight through the slab, which would have a certain diameter (imaged using the high-resolution plane) and an ‘infinite’ elongation (in the low-resolution direction). However, the vessels targeted here can have any orientation and curvature; an anisotropic acquisition could therefore introduce a bias favouring vessels with a particular orientation relative to the voxel grid. Note that the same argument applies when answering the question why a further reduction slab thickness would eventually result in less increase in FRE (section Introducing a partial-volume model). We have added a corresponding comment in our discussion on practical imaging considerations:

"In summary, numerous theoretical and practical considerations remain for optimal imaging of pial arteries using time-of-flight contrast. Depending on the application, advanced displacement artefact compensation strategies may be required, and zero-filling could provide better vessel depiction. Further, an optimal trade-off between SNR, voxel size and acquisition time needs to be found. Currently, the partial-volume FRE model only considers voxel size, and—as we reduced the voxel size in the experiments—we (partially) compensated the reduction in SNR through longer scan times. This, ultimately, also required the use of prospective motion correction to enable the very long acquisition times necessary for 140 µm isotropic voxel size. Often, anisotropic voxels are used to reduce acquisition time and increase SNR while maintaining in-plane resolution. This may indeed prove advantageous when the (also highly anisotropic) arteries align with the anisotropic acquisition, e.g. when imaging the large supplying arteries oriented mostly in the head-foot direction. In the case of pial arteries, however, there is not preferred orientation because of the convoluted nature of the pial arterial vasculature encapsulating the complex folding of the cortex (see section Anatomical architecture of the pial arterial vasculature). A further reduction in voxel size may be possible in dedicated research settings utilizing even longer acquisition times and a larger field-of-view to maintain SNR. However, if acquisition time is limited, voxel size and SNR need to be carefully balanced against each other."

Reviewer #2 (Public Review):

Overview

This paper explores the use of inflow contrast MRI for imaging the pial arteries. The paper begins by providing a thorough background description of pial arteries, including past studies investigating the velocity and diameter. Following this, the authors consider this information to optimize the contrast between pial arteries and background tissue. This analysis reveals spatial resolution to be a strong factor influencing the contrast of the pial arteries. Finally, experiments are performed on a 7T MRI to investigate: the effect of spatial resolution by acquiring images at multiple resolutions, demonstrate the feasibility of acquiring ultrahigh resolution 3D TOF, the effect of displacement artifacts, and the prospect of using T2* to remove venous voxels.

Impression

There is certainly interest in tools to improve our understanding of the architecture of the small vessels of the brain and this work does address this. The background description of the pial arteries is very complete and the manuscript is very well prepared. The images are also extremely impressive, likely benefiting from motion correction, 7T, and a very long scan time. The authors also commit to open science and provide the data in an open platform. Given this, I do feel the manuscript to be of value to the community; however, there are concerns with the methods for optimization, the qualitative nature of the experiments, and conclusions drawn from some of the experiments.

Specific Comments :

1) Figure 3 and Theory surrounding. The optimization shown in Figure 3 is based fixing the flip angle or the TR. As is well described in the literature, there is a strong interdependency of flip angle and TR. This is all well described in literature dating back to the early 90s. While I think it reasonable to consider these effects in optimization, the language needs to include this interdependency or simply reference past work and specify how the flip angle was chosen. The human experiments do not include any investigation of flip angle or TR optimization.

We thank the reviewer for raising this valuable point, and we fully agree that there is an interdependency between these two parameters. To simplify our optimization, we did fix one parameter value at a time, but in the revised manuscript we clarified that both parameters can be optimized simultaneously. Importantly, a large range of parameter values will result in a similar FRE in the small artery regime, which is illustrated in the optimization provided in the main text. We have therefore chosen the repetition time based on encoding efficiency and then set a corresponding excitation flip angle. In addition, we have also provided additional simulations in the supplementary material outlining the interdependency for the case of pial arteries.

"Optimization of repetition time and excitation flip angle

As the main goal of the optimisation here was to start within an already established parameter range for TOF imaging at ultra-high field (Kang et al., 2010; Stamm et al., 2013; von Morze et al., 2007), we only needed to then further tailor these for small arteries by considering a third parameter, namely the blood delivery time. From a practical perspective, a TR of 20 ms as a reference point was favourable, as it offered a time-efficient readout minimizing wait times between excitations but allowing low encoding bandwidths to maximize SNR. Due to the interdependency of flip angle and repetition time, for any one blood delivery time any FRE could (in theory) be achieved. For example, a similar FRE curve at 18 ° flip angle and 5 ms TR can also be achieved at 28 ° flip angle and 20 ms TR; or the FRE curve at 18 ° flip angle and 30 ms TR is comparable to the FRE curve at 8 ° flip angle and 5 ms TR (Supplementary Figure 3 TOP). In addition, the difference between optimal parameter settings diminishes for long blood delivery times, such that at a blood delivery time of 500 ms (Supplementary Figure 3 BOTTOM), the optimal flip angle at a TR of 15 ms, 20 ms or 25 ms would be 14 °, 16 ° and 18 °, respectively. This is in contrast to a blood delivery time of 100 ms, where the optimal flip angles would be 32 °, 37 ° and 41 °. In conclusion, in the regime of small arteries, long TR values in combination with low flip angles ensure flow-related enhancement at blood delivery times of 200 ms and above, and within this regime there are marginal gains by further optimizing parameter values and the optimal values are all similar."

Supplementary Figure 3: Optimal imaging parameters for small arteries. This assessment follows the simulations presented in Figure 3, but in addition shows the interdependency for the corresponding third parameter (either flip angle or repetition time). TOP: Flip angles close to the Ernst angle show only a marginal flow-related enhancement; however, the influence of the blood delivery time decreases further (LEFT). As the flip angle increases well above the values used in this study, the flow-related enhancement in the small artery regime remains low even for the longer repetition times considered here (RIGHT). BOTTOM: The optimal excitation flip angle shows reduced variability across repetition times in the small artery regime compared to shorter blood delivery times.

"Based on these equations, optimal T_R and excitation flip angle values (θ) can be calculated for the blood delivery times under consideration (Figure 3). To better illustrate the regime of small arteries, we have illustrated the effect of either flip angle or T_R while keeping the other parameter values fixed to the value that was ultimately used in the experiments; although both parameters can also be optimized simultaneously (Haacke et al., 1990). Supplementary Figure 3 further delineates the interdependency between flip angle and T_R within a parameter range commonly used for TOF imaging at ultra-high field (Kang et al., 2010; Stamm et al., 2013; von Morze et al., 2007). Note how longer T_R values still provide an FRE effect even at very long blood delivery times, whereas using shorter T_R values can suppress the FRE effect (Figure 3, left). Similarly, at lower flip angles the FRE effect is still present for long blood delivery times, but it is not available anymore at larger flip angles, which, however, would give maximum FRE for shorter blood delivery times (Figure 3, right). Due to the non-linear relationships of both blood delivery time and flip angle with FRE, the optimal imaging parameters deviate considerably when comparing blood delivery times of 100 ms and 300 ms, but the differences between 300 ms and 1000 ms are less pronounced. In the following simulations and measurements, we have thus used a T_R value of 20 ms, i.e. a value only slightly longer than the readout of the high-resolution TOF acquisitions, which allowed time-efficient data acquisition, and a nominal excitation flip angle of 18°. From a practical standpoint, these values are also favorable as the low flip angle reduces the specific absorption rate (Fiedler et al., 2018) and the long T_R value decreases the potential for peripheral nerve stimulation (Mansfield and Harvey, 1993)."

2) Figure 4 and Theory surrounding. A major limitation of this analysis is the lack of inclusion of noise in the analysis. I believe the results to be obvious that the FRE will be modulated by partial volume effects, here described quadratically by assuming the vessel to pass through the voxel. This would substantially modify the analysis, with a shift towards higher voxel volumes (scan time being equal). The authors suggest the FRE to be the dominant factor effecting segmentation; however, segmentation is limited by noise as much as contrast.

We of course agree with the reviewer that contrast-to-noise ratio is a key factor that determines the detection of vessels and the quality of the segmentation, however there are subtleties regarding the exact inter-relationship between CNR, resolution, and segmentation performance.

The main purpose of Figure 4 is not to provide a trade-off between flow-related enhancement and signal-to-noise ratio—in particular as SNR is modulated by many more factors than voxel size alone, e.g. acquisition time, coil geometry and instrumentation—but to decide whether the limiting factor for imaging pial arteries is the reduction in flow-related enhancement due to long blood delivery times (which is the explanation often found in the literature (Chen et al., 2018; Haacke et al., 1990; Masaryk et al., 1989; Mut et al., 2014; Park et al., 2020; Parker et al., 1991; Wilms et al., 2001; Wright et al., 2013)) or due to partial volume effects. Furthermore, when reducing voxel size one will also likely increase the number of encoding steps to maintain the imaging coverage (i.e., the field-of-view) and so the relationship between voxel size and SNR in practice is not straightforward. Therefore, we had to conclude that deducing a meaningful SNR analysis that would benefit the reader was not possible given the available data due to the complex relationship between voxel size and other imaging parameters. Note that these considerations are not specific to imaging the pial arteries but apply to all MRA acquisitions, and have thus been discussed previously in the literature. Here, we wanted to focus on the novel insights gained in our study, namely that it provides an expression for how relative FRE contrast changes with voxel size with some assumptions that apply for imaging pial arteries.

Further, depending on the definition of FRE and whether partial-volume effects are included (see also our response to R2.8), larger voxel volumes have been found to be theoretically advantageous even when only considering contrast (Du et al., 1996; Venkatesan and Haacke, 1997), which is not in line with empirical observations (Al-Kwifi et al., 2002; Bouvy et al., 2014; Haacke et al., 1990; Ladd, 2007; Mattern et al., 2018; von Morze et al., 2007).

The notion that vessel segmentation algorithms perform well on noisy data but poorly on low-contrast data was mainly driven by our own experiences. However, we still believe that the assumption that (all) segmentation algorithms are linearly dependent on contrast and noise (which the formulation of a contrast-to-noise ratio presumes) is similarly not warranted. Indeed, the necessary trade-off between FRE and SNR might be specific to the particular segmentation algorithm being used than a general property of the acquisition. Please also note that our analysis of the FRE does not suggest that an arbitrarily high resolution is needed. Importantly, while we previously noted that reducing voxel size improves contrast in vessels whose diameters are smaller than the voxel size, we now explicitly acknowledge that, for vessels whose diameters are larger than the voxel size reducing the voxel size is not helpful---since it only reduces SNR without any gain in contrast---and may hinder segmentation performance, and thus become counterproductive. But we take the reviewer’s point and also acknowledge that these intricacies need to be mentioned, and therefore we have rephrased the statement in the discussion in the following way:

"In general, we have not considered SNR, but only FRE, i.e. the (relative) image contrast, assuming that segmentation algorithms would benefit from higher contrast for smaller arteries. Importantly, the acquisition parameters available to maximize FRE are limited, namely repetition time, flip angle and voxel size. SNR, however, can be improved via numerous avenues independent of these parameters (Brown et al., 2014b; Du et al., 1996; Heverhagen et al., 2008; Parker et al., 1991; Triantafyllou et al., 2011; Venkatesan and Haacke, 1997), the simplest being longer acquisition times. If the aim is to optimize a segmentation outcome for a given acquisition time, the trade-off between contrast and SNR for the specific segmentation algorithm needs to be determined (Klepaczko et al., 2016; Lesage et al., 2009; Moccia et al., 2018; Phellan and Forkert, 2017). Our own—albeit limited—experience has shown that segmentation algorithms (including manual segmentation) can accommodate a perhaps surprising amount of noise using prior knowledge and neighborhood information, making these high-resolution acquisitions possible. Importantly, note that our treatment of the FRE does not suggest that an arbitrarily small voxel size is needed, but instead that voxel sizes appropriate for the arterial diameter of interest are beneficial (in line with the classic “matched-filter” rationale (North, 1963)). Voxels smaller than the arterial diameter would not yield substantial benefits (Figure 5) and may result in SNR reductions that would hinder segmentation performance."

3) Page 11, Line 225. "only a fraction of the blood is replaced" I think the language should be reworded. There are certainly water molecules in blood which have experience more excitation B1 pulses due to the parabolic flow upstream and the temporal variation in flow. There is magnetization diffusion which reduces the discrepancy; however, it seems pertinent to just say the authors assume the signal is represented by the average arrival time. This analysis is never verified and is only approximate anyways. The "blood dwell time" is also an average since voxels near the wall will travel more slowly. Overall, I recommend reducing the conjecture in this section.

We fully agree that our treatment of the blood dwell time does not account for the much more complex flow patterns found in cortical arteries. However, our aim was not do comment on these complex patterns, but to help establish if, in the simplest scenario assuming plug flow, the often-mentioned slow blood flow requires multiple velocity compartments to describe the FRE (as is commonly done for 2D MRA (Brown et al., 2014a; Carr and Carroll, 2012)). We did not intend to comment on the effects of laminar flow or even more complex flow patterns, which would require a more in-depth treatment. However, as the small arteries targeted here are often just one voxel thick, all signals are indeed integrated within that voxel (i.e. there is no voxel near the wall that travels more slowly), which may average out more complex effects. We have clarified the purpose and scope of this section in the following way:

"In classical descriptions of the FRE effect (Brown et al., 2014a; Carr and Carroll, 2012), significant emphasis is placed on the effect of multiple “velocity segments” within a slice in the 2D imaging case. Using the simplified plug-flow model, where the cross-sectional profile of blood velocity within the vessel is constant and effects such as drag along the vessel wall are not considered, these segments can be described as ‘disks’ of blood that do not completely traverse through the full slice within one T_R, and, thus, only a fraction of the blood in the slice is replaced. Consequently, estimation of the FRE effect would then need to accommodate contribution from multiple ‘disks’ that have experienced 1 to k RF pulses. In the case of 3D imaging as employed here, multiple velocity segments within one voxel are generally not considered, as the voxel sizes in 3D are often smaller than the slice thickness in 2D imaging and it is assumed that the blood completely traverses through a voxel each T_R. However, the question arises whether this assumption holds for pial arteries, where blood velocity is considerably lower than in intracranial vessels (Figure 2). To answer this question, we have computed the blood dwell time , i.e. the average time it takes the blood to traverse a voxel, as a function of blood velocity and voxel size (Figure 2). For reference, the blood velocity estimates from the three studies mentioned above (Bouvy et al., 2016; Kobari et al., 1984; Nagaoka and Yoshida, 2006) have been added in this plot as horizontal white lines. For the voxel sizes of interest here, i.e. 50–300 μm, blood dwell times are, for all but the slowest flows, well below commonly used repetition times (Brown et al., 2014a; Carr and Carroll, 2012; Ladd, 2007; von Morze et al., 2007). Thus, in a first approximation using the plug-flow model, it is not necessary to include several velocity segments for the voxel sizes of interest when considering pial arteries, as one might expect from classical treatments, and the FRE effect can be described by equations (1) – (3), simplifying our characterization of FRE for these vessels. When considering the effect of more complex flow patterns, it is important to bear in mind that the arteries targeted here are only one-voxel thick, and signals are integrated across the whole artery."

4) Page 13, Line 260. "two-compartment modelling" I think this section is better labeled "Extension to consider partial volume effects" The compartments are not interacting in any sense in this work.

Thank you for this suggestion. We have replaced the heading with Introducing a partial-volume model (page 14) and replaced all instances of ‘two-compartment model’ with ‘partial-volume model’.

5) Page 14, Line 284. "In practice, a reduction in slab …." "reducing the voxel size is a much more promising avenue" There is a fair amount on conjecture here which is not supported by experiments. While this may be true, the authors also use a classical approach with quite thin slabs.

The slab thickness used in our experiments was mainly limited by the acquisition time and the participants ability to lie still. We indeed performed one measurement with a very experienced participant with a thicker slab, but found that with over 20 minutes acquisition time, motion artefacts were unavoidable. The data presented in Figure 5 were acquired with similar slab thickness, supporting the statement that reducing the voxel size is a promising avenue for imaging small pial arteries. However, we indeed have not provided an empirical comparison of the effect of slab thickness. Nevertheless, we believe it remains useful to make the theoretical argument that due to the convoluted nature of the pial arterial vascular geometry, a reduction in slab thickness may not reduce the acquisition time if no reduction in intra-slab vessel length can be achieved, i.e. if the majority of the artery is still contained in the smaller slab. We have clarified the statement and removed the direct comparison (‘much more’ promising) in the following way:

"In theory, a reduction in blood delivery time increases the FRE in both regimes, and—if the vessel is smaller than the voxel—so would a reduction in voxel size. In practice, a reduction in slab thickness―which is the default strategy in classical TOF-MRA to reduce blood delivery time―might not provide substantial FRE increases for pial arteries. This is due to their convoluted geometry (see section Anatomical architecture of the pial arterial vasculature), where a reduction in slab thickness may not necessarily reduce the vessel segment length if the majority of the artery is still contained within the smaller slab. Thus, given the small arterial diameter, reducing the voxel size is a promising avenue when imaging the pial arterial vasculature."

6) Figure 5. These image differences are highly exaggerated by the lack of zero filling (or any interpolation) and the fact that the wildly different. The interpolation should be addressed, and the scan time discrepancy listed as a limitation.

We have extended the discussion around zero-filling by including additional considerations based on the imaging parameters in Figure 5 and highlighted the substantial differences in voxel volume. Our choice not to perform zero-filling was driven by the open question of what an ‘optimal’ zero-filling factor would be. We have also highlighted the substantial differences in acquisition time when describing the results.

Changes made to the results section:

"To investigate the effect of voxel size on vessel FRE, we acquired data at four different voxel sizes ranging from 0.8 mm to 0.3 mm isotropic resolution, adjusting only the encoding matrix, with imaging parameters being otherwise identical (FOV, TR, TE, flip angle, R, slab thickness, see section Data acquisition). The total acquisition time increases from less than 2 minutes for the lowest resolution scan to over 6 minutes for the highest resolution scan as a result."

Changes made to the discussion section:

"Nevertheless, slight qualitative improvements in image appearance have been reported for higher zero-filling factors (Du et al., 1994), presumably owing to a smoother representation of the vessels (Bartholdi and Ernst, 1973). In contrast, Mattern et al. (2018) reported no improvement in vessel contrast for their high-resolution data. Ultimately, for each application, e.g. visual evaluation vs. automatic segmentation, the optimal zero-filling factor needs to be determined, balancing image appearance (Du et al., 1994; Zhu et al., 2013) with loss in statistical independence of the image noise across voxels. For example, in Figure 5, when comparing across different voxel sizes, the visual impression might improve with zero-filling. However, it remains unclear whether the same zero-filling factor should be applied for each voxel size, which means that the overall difference in resolution remains, namely a nearly 20-fold reduction in voxel volume when moving from 0.8-mm isotropic to 0.3-mm isotropic voxel size. Alternatively, the same ’zero-filled’ voxel sizes could be used for evaluation, although then nearly 94 % of the samples used to reconstruct the image with 0.8-mm voxel size would be zero-valued for a 0.3-mm isotropic resolution. Consequently, all data presented in this study were reconstructed without zero-filling."

7) Figure 7. Given the limited nature of experiment may it not also be possible the subject moved more, had differing brain blood flow, etc. Were these lengthy scans acquired in the same session? Many of these differences could be attributed to other differences than the small difference in spatial resolution.

The scans were acquired in the same session using the same prospective motion correction procedure. Note that the acquisition time of the images with 0.16 mm isotropic voxel size was comparatively short, taking just under 12 minutes. Although the difference in spatial resolution may seem small, it still amounts to a 33% reduction in voxel volume. For comparison, reducing the voxel size from 0.4 mm to 0.3 mm also ‘only’ reduces the voxel volume by 58 %—not even twice as much. Overall, we fully agree that additional validation and optimisation of the imaging parameters for pial arteries are beneficial and have added a corresponding statement to the Discussion section.

Changes made to the results section (also in response to Reviewer 1 (R1.22))

"We have also acquired one single slab with an isotropic voxel size of 0.16 mm with prospective motion correction for this participant in the same session to compare to the acquisition with 0.14 mm isotropic voxel size and to test whether any gains in FRE are still possible at this level of the vascular tree."

Changes made to the discussion section:

"Acquiring these data at even higher field strengths would boost SNR (Edelstein et al., 1986; Pohmann et al., 2016) to partially compensate for SNR losses due to acceleration and may enable faster imaging and/or smaller voxel sizes. This could facilitate the identification of the ultimate limit of the flow-related enhancement effect and identify at which stage of the vascular tree does the blood delivery time become the limiting factor. While Figure 7 indicates the potential for voxel sizes below 0.16 mm, the singular nature of this comparison warrants further investigations."

8) Page 22, Line 395. Would the analysis be any different with an absolute difference? The FRE (Eq 6) divides by a constant value. Clearly there is value in the difference as other subtractive inflow imaging would have infinite FRE (not considering noise as the authors do).

Absolutely; using an absolute FRE would result in the highest FRE for the largest voxel size, whereas in our data small vessels are more easily detected with the smallest voxel size. We also note that relative FRE would indeed become infinite if the value in the denominator representing the tissue signal was zero, but this special case highlights how relative FRE can help characterize “segmentability”: a vessel with any intensity surrounded by tissue with an intensity of zero is trivially/infinitely segmentatble. We have added this point to the revised manuscript as indicated below.

Following the suggestion of Reviewer 1 (R1.2), we have included additional simulations to clarify the effects of relative FRE definition and partial-volume model, in which we show that only when considering both together are smaller voxel sizes advantageous (Supplementary Material).

"Effect of FRE Definition and Interaction with Partial-Volume Model

For the definition of the FRE effect in this study, we used a measure of relative FRE (Al-Kwifi et al., 2002) in combination with a partial-volume model (Eq. 6). To illustrate the effect of these two definitions, as well as their interaction, we have estimated the relative and absolute FRE for an artery with a diameter of 200 µm and 2 000 µm (i.e. no partial-volume effects). The absolute FRE explicitly takes the voxel volume into account, i.e. instead of Eq. (6) for the relative FRE we used"

Eq. (1)

Note that the division by

to obtain the relative FRE removes the contribution of the total voxel volume

"Supplementary Figure 2 shows that, when partial volume effects are present, the highest relative FRE arises in voxels with the same size as or smaller than the vessel diameter (Supplementary Figure 2A), whereas the absolute FRE increases with voxel size (Supplementary Figure 2C). If no partial-volume effects are present, the relative FRE becomes independent of voxel size (Supplementary Figure 2B), whereas the absolute FRE increases with voxel size (Supplementary Figure 2D). While the partial-volume effects for the relative FRE are substantial, they are much more subtle when using the absolute FRE and do not alter the overall characteristics."

Supplementary Figure 2: Effect of voxel size and blood delivery time on the relative flow-related enhancement (FRE) using either a relative (A,B) (Eq. (3)) or an absolute (C,D) (Eq. (12)) FRE definition assuming a pial artery diameter of 200 μm (A,C) or 2 000 µm, i.e. no partial-volume effects at the central voxel of this artery considered here.

Following the established literature (Brown et al., 2014a; Carr and Carroll, 2012; Haacke et al., 1990) and because we would ultimately derive a relative measure, we have omitted the effect of voxel volume on the longitudinal magnetization in our derivations, which make it appear as if we are dividing by a constant in Eq. 6, as the effect of total voxel volume cancels out for the relative FRE. We have now made this more explicit in our derivation of the partial volume model.

"Introducing a partial-volume model

To account for the effect of voxel volume on the FRE, the total longitudinal magnetization M_z needs to also consider the number of spins contained within in a voxel (Du et al., 1996; Venkatesan and Haacke, 1997). A simple approximation can be obtained by scaling the longitudinal magnetization with the voxel volume (Venkatesan and Haacke, 1997) . To then include partial volume effects, the total longitudinal magnetization in a voxel M_z^total becomes the sum of the contributions from the stationary tissue M_zS^tissue and the inflowing blood M_z^blood, weighted by their respective volume fractions V_rel:"

A simple approximation can be obtained by scaling the longitudinal magnetization with the voxel volume (Venkatesan and Haacke, 1997) . To then include partial volume effects, the total longitudinal magnetization in a voxel M_z^total becomes the sum of the contributions from the stationary tissue M_zS^tissue and the inflowing blood M_z^blood, weighted by their respective volume fractions V_rel:

Eq. (4)

For simplicity, we assume a single vessel is located at the center of the voxel and approximate it to be a cylinder with diameter d_vessel and length l_voxel of an assumed isotropic voxel along one side. The relative volume fraction of blood V_rel^blood is the ratio of vessel volume within the voxel to total voxel volume (see section Estimation of vessel-volume fraction in the Supplementary Material), and the tissue volume fraction V_rel^tissue is the remainder that is not filled with blood, or

Eq. (5)

We can now replace the blood magnetization in equation Eq. (3) with the total longitudinal magnetization of the voxel to compute the FRE as a function of vessel-volume fraction:

Eq. (6)

Based on your suggestion, we have also extended our interpretation of relative and absolute FRE. Indeed, a subtractive flow technique where no signal in the background remains and only intensities in the object are present would have infinite relative FRE, as this basically constitutes a perfect segmentation (bar a simple thresholding step).

"Extending classical FRE treatments to the pial vasculature

There are several major modifications in our approach to this topic that might explain why, in contrast to predictions from classical FRE treatments, it is indeed possible to image pial arteries. For instance, the definition of vessel contrast or flow-related enhancement is often stated as an absolute difference between blood and tissue signal (Brown et al., 2014a; Carr and Carroll, 2012; Du et al., 1993, 1996; Haacke et al., 1990; Venkatesan and Haacke, 1997). Here, however, we follow the approach of Al-Kwifi et al. (2002) and consider relative contrast. While this distinction may seem to be semantic, the effect of voxel volume on FRE for these two definitions is exactly opposite: Du et al. (1996) concluded that larger voxel size increases the (absolute) vessel-background contrast, whereas here we predict an increase in relative FRE for small arteries with decreasing voxel size. Therefore, predictions of the depiction of small arteries with decreasing voxel size differ depending on whether one is considering absolute contrast, i.e. difference in longitudinal magnetization, or relative contrast, i.e. contrast differences independent of total voxel size. Importantly, this prediction changes for large arteries where the voxel contains only vessel lumen, in which case the relative FRE remains constant across voxel sizes, but the absolute FRE increases with voxel size (Supplementary Figure 9). Overall, the interpretations of relative and absolute FRE differ, and one measure may be more appropriate for certain applications than the other. Absolute FRE describes the difference in magnetization and is thus tightly linked to the underlying physical mechanism. Relative FRE, however, describes the image contrast and segmentability. If blood and tissue magnetization are equal, both contrast measures would equal zero and indicate that no contrast difference is present. However, when there is signal in the vessel and as the tissue magnetization approaches zero, the absolute FRE approaches the blood magnetization (assuming no partial-volume effects), whereas the relative FRE approaches infinity. While this infinite relative FRE does not directly relate to the underlying physical process of ‘infinite’ signal enhancement through inflowing blood, it instead characterizes the segmentability of the image in that an image with zero intensity in the background and non-zero values in the structures of interest can be segmented perfectly and trivially. Accordingly, numerous empirical observations (Al-Kwifi et al., 2002; Bouvy et al., 2014; Haacke et al., 1990; Ladd, 2007; Mattern et al., 2018; von Morze et al., 2007) and the data provided here (Figure 5, 6 and 7) have shown the benefit of smaller voxel sizes if the aim is to visualize and segment small arteries."

9) Page 22, Line 400. "The appropriateness of " This also ignores noise. The absolute enhancement is the inherent magnetization available. The results in Figure 5, 6, 7 don't readily support a ratio over and absolute difference accounting for partial volume effects.

We hope that with the additional explanations on the effects of relative FRE definition in combination with a partial-volume model and the interpretation of relative FRE provided in the previous response (R2.8) and that Figures 5, 6 and 7 show smaller arteries for smaller voxels, we were able to clarify our argument why only relative FRE in combination with a partial volume model can explain why smaller voxel sizes are advantageous for depicting small arteries.

While we appreciate that there exists a fundamental relationship between SNR and voxel volume in MR (Brown et al., 2014b), this relationship is also modulated by many more factors (as we have argued in our responses to R2.2 and R1.4b).

We hope that the additional derivations and simulations provided in the previous response have clarified why a relative FRE model in combination with a partial-volume model helps to explain the enhanced detectability of small vessels with small voxels.

10) Page 24, Line 453. "strategies, such as radial and spiral acquisitions, experience no vessel displacement artefact" These do observe flow related distortions as well, just not typically called displacement.

Yes, this is a helpful point, as these methods will also experience a degradation of spatial accuracy due to flow effects, which will propagate into errors in the segmentation.

As the reviewer suggests, flow-related artefacts in radial and spiral acquisitions usually manifest as a slight blur, and less as the prominent displacement found in Cartesian sampling schemes. We have added a corresponding clarification to the Discussion section:

"Other encoding strategies, such as radial and spiral acquisitions, experience no vessel displacement artefact because phase and frequency encoding take place in the same instant; although a slight blur might be observed instead (Nishimura et al., 1995, 1991). However, both trajectories pose engineering challenges and much higher demands on hardware and reconstruction algorithms than the Cartesian readouts employed here (Kasper et al., 2018; Shu et al., 2016); particularly to achieve 3D acquisitions with 160 µm isotropic resolution."

11) Page 24, Line 272. "although even with this nearly ideal subject behaviour approximately 1 in 4 scans still had to be discarded and repeated" This is certainly a potential source of bias in the comparisons.

We apologize if this section was written in a misleading way. For the comparison presented in Figure 7, we acquired one additional slab in the same session at 0.16 mm voxel size using the same prospective motion correction procedure as for the 0.14 mm data. For the images shown in Figure 6 and Supplementary Figure 4 at 0.16 mm voxel size, we did not use a motion correction system and, thus, had to discard a portion of the data. We have clarified that for the comparison of the high-resolution data, prospective motion correction was used for both resolutions. We have clarified this in the Discussion section:

"This allowed for the successful correction of head motion of approximately 1 mm over the 60-minute scan session, showing the utility of prospective motion correction at these very high resolutions. Note that for the comparison in Figure 7, one slab with 0.16 mm voxel size was acquired in the same session also using the prospective motion correction system. However, for the data shown in Figure 6 and Supplementary Figure 4, no prospective motion correction was used, and we instead relied on the experienced participants who contributed to this study. We found that the acquisition of TOF data with 0.16 mm isotropic voxel size in under 12 minutes acquisition time per slab is possible without discernible motion artifacts, although even with this nearly ideal subject behaviour approximately 1 in 4 scans still had to be discarded and repeated."

12) Page 25, Line 489. "then need to include the effects of various analog and digital filters" While the analysis may benefit from some of this, most is not at all required for analysis based on optimization of the imaging parameters.

We have included all four correction factors for completeness, given the unique acquisition parameter and contrast space our time-of-flight acquisition occupies, e.g. very low bandwidth of only 100 Hz, very large matrix sizes > 1024 samples, ideally zero SNR in the background (fully supressed tissue signal). However, we agree that probably the most important factor is the non-central chi distribution of the noise in magnitude images from multiple-channel coil arrays, and have added this qualification in the text:

"Accordingly, SNR predictions then need to include the effects of various analog and digital filters, the number of acquired samples, the noise covariance correction factor, and—most importantly—the non-central chi distribution of the noise statistics of the final magnitude image (Triantafyllou et al., 2011)."

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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 #1 (Public Review):

The data support the claims, and the manuscript does not have significant weaknesses in its present form. Key strengths of the paper include using a creative HR-based reporter system combining different inducible DSB positions along a chromosome arm and testing plasmid-based and chromosomal donor sequences. Combining that system with the visualization of specific chromosomal sites via microscopy is powerful. Overall, this work will constitute a timely and helpful contribution to the field of DSB/genome mobility in DNA repair, especially in yeast, and may inform similar mechanisms in other organisms. Importantly, this study also reconciles some of the apparent contradictions in the field.

We thank the reviewer for these positive comments on the quality of the THRIV system, in helping us to understand global mobility and to reconcile the different studies in the field. The possibility that these mobilities also exist in other organisms is attractive because they could be a way to anticipate the position of the damage in the genome and its possible outcome.

Reviewer #2 (Public Review):

The authors are clarifying the role of global mobility in homologous recombination (HR). Global mobility is positively correlated with recombinant product formation in some reports. However, some studies argue the contrary and report that global mobility is not essential for HR. To characterize the role of global chromatin mobility during HR, the authors set up a system in haploid yeast cells that allows simultaneously tracking of HR at the single-cell level and allows the analysis of different positions of the DSB induction. By moving the position of the DSB within their system, the authors postulate that the chromosomal conformation surrounding a DNA break affects the global mobility response. Finally, the authors assessed the contributions of H2A(X) phosphorylation, checkpoint progression and Rad51 in the mobility response.

One of the strengths of the manuscript is the development of "THRIV" as an efficient method for tracking homologous recombination in vivo. The authors take advantage of the power of yeast genetics and use gene deletions and as well as mutations to test the contribution of H2A(X) phosphorylation, checkpoint progression and Rad51 to the mobility response in their THRIV system.

A major weakness in the manuscript is the lack of a marker to indicate that DSB formation has occurred (or is occurring)? Although at 6 hours there is 80% I-SceI cutting, around 20% of the cells are uncut and cannot be distinguished from the ones that are cut (or have already been repaired). Thus, the MSD analysis is done in the blind with respect to cells actually undergoing DSB repair.

The authors clearly outlined their aims and have substantial evidence to support their conclusions. They discovered new features of global mobility that may clear up some of the controversies in the field. They overinterpreted some of their observations, but these criticisms can be easily addressed.

The authors addressed conflicting results concerning the importance of global mobility to HR and their results aid in reconciling some of the controversies in the field. A key strength of this manuscript is the analysis of global mobility in response to breaks at different locations within chromosomes? They identified two types of DSB-induced global chromatin mobility involved in HR and postulate that they differ based on the position of the DSB. For example, DSBs close to the centromere exhibit increased global mobility that is not essential for repair and depends solely on H2A(X) phosphorylation. However, if the DSB is far away from the centromere, then global mobility is essential for HR and is dependent on H2A(X) phosphorylation, checkpoint progression as well as the Rad51 recombinase.

The Bloom lab had previously identified differences in mobility based on the position of the tracked site. However, in the study reported here, the mobility response is analyzed after inducing DSBs located at different positions along the chromosome.

They also addressed the question of the importance of the Rad51 protein in increased global mobility in haploid cells. Previous studies used DNA damaging agents that induce DSBs randomly throughout the genome, where it would have been rare to induce DSBs near the centromere. In the studies reported in this manuscript, they find no increase in global mobility in a rad51∆ background for breaks induced near the centromere (proximal), but find that breaks induced near the telomeres (distal), are dependent on both gamma-H2A(X) spreading and the Rad51 recombinase.

We thank the referee for his constructive comments on the strength of our system to accurately determine the impact of a DSB according to its position in the genome. Concerning the issue of damaged cells that were not detected, it is a very important and exciting issue because it confronts our data with the question of biological heterogeneity. We provide evidence on the consistency of our findings despite the lack of detection of undamaged cells.

Reviewer #3 (Public Review):

In this study, Garcia Fernandez et al. employ a variety of genetic constructs to define the mechanism underlying the global chromatin mobility elicited in response to a single DNA double-strand break (DSB). Such local and global chromatin mobility increases have been described a decade ago by the Gasser and Rothstein laboratories, and a number of determinants have been identified: one epistasis group results in H2A-S129 phosphorylation via Rad9 and Mec1 activation. The mechanism is thought to be due to chromatin rigidification (Herbert 2017; Miné-Hattab 2017) or general eviction of histones (Cheblal 2020). More enigmatic, global chromatin mobility increase also depends on Rad51, a central recombination protein downstream of checkpoint activation (Smith & Rothstein 2017), which is also required for local DSB mobility (Dion .. Gasser 2012). The authors set out to address this difficulty in the field.

A premise of their study is the convergence of two types of observations: First, the H2A phosphorylation ChIP profile matches that of Rad51, with both spreading in trans on other chromosomes at the level of centromeres when a DSB occurs in the vicinity of one of them (Renkawitz 2014). Second, global mobility depends on H2A phosphorylation and on Rad51 (their previous study Herbert 2017). They thus address whether the Rad51-ssDNA filament (and associated proteins) marks the chromatin engaged during the homology search. They found that the extent of the mobility depends on the residency time of the filament in a particular genomic and nuclear region, which can be induced at an initially distant trans site by providing a region of homology. Unfortunately, these findings are not clearly apparent from the title and the abstract, and in fact somewhat misrepresented in the manuscript, which would call for a rewrite (see points below).

The main goal of our study was to understand the role of global mobility in the repair by homologous recombination, depending on the location of the damage. We found distinct global mobility mechanisms, in particular in the involvement of the Rad51 nucleofilament, depending on whether the DSB was pericentromeric or not. It is thus likely that when the DSB is far from the pericentromere, the residence time of the Rad51 nucleofilament with the donor has an impact on global mobility. Thus, if our experiments were not designed to answer directly the question of the residence time of the nucleofilament, we now discuss in more detail the causes and consequences of the global mobility.

To this end, they induce the formation of a site-specific DSB in either of two regions: a centromere-proximal region and a telomere-proximal region, and measure the mobility of an undamaged site near the centromere on another chromosome (with a LacO-LacI-GFP system). This system reveals that only the centromere-proximal DSB induces the mobility of the centromere-proximal undamaged site, in a Rad9- and Rad51-independent manner. Providing a homologous donor in the vicinity of the LacO array (albeit in trans) restores its mobility when the DSB is located in a subtelomeric region, in a Rad9- and Rad51-dependent fashion. These genetic requirements are the same as those described for local DSB mobility (Dion & Gasser 2012), drawing a link between the two types of mobility, which to my knowledge was not described. The authors should focus their message (too scattered in the current manuscript), on these key findings and the diffusive "painting" model, in which the canvas is H2A, the moving paintbrush Mec1, and the hand the Rad51-ssDNA filament whose movement depends on Rad9. In the absence of Rad51-Rad9 the hand stays still, only decorating H2A in its immediate environment. The amount of paint deposited depends on the residency time of the Rad51-ssDNA-Mec1 filament in a given nuclear region. This synthesis is in agreement with the data presented and contrasts with their proposal that "two types of global mobility" exist.

The brush model is very useful in explaining the distal mobility, which indeed is linked to local mobility genetic requirements, but it is also helpful to think of different model than the brush model when pericentromeric damage occurs. To stay in the terms of painting technique, this model would be similar to the pouring technique, when oil paint is deposited on water and spreads in a multidirectional manner. It is likely that Mec1 or Tel1 are the factors responsible for this spreading pattern. We therefore propose to maintain the notion of two distinct types of mobilities. Without going into pictorial techniques in the text, we have attempted to clarify these two models in the manuscript.

The rest of the manuscript attempts to define a role in DSB repair of this phosphor-H2A-dependent mobility, using a fluorescence recovery assay upon DSB repair. They correlate a defect in the centromere-proximal mobility (in the rad9 or h2a-s129a mutant) when a DSB is distantly induced in the subtelomere with a defect in repairing the DSB. Repair efficiency is not affected by these mutations when the donor is located initially close to the DSB site. This part is less convincing, as repair failure specifically at a distant donor in the rad9 and H2A-S129A mutants may result from other defects relating to chromatin than its mobility (i.e. affecting homology sampling, DNA strand invasion, D-loop extension, D-loop disruption, etc), which could be partially alleviated by repeated DSB-donor encounters when the two are spatially close. In fact, suggesting that undamaged site mobility is required for the early step of the homology search directly contradicts the fact that the centromere-proximal mobility induced by a subtelomeric DSB depends on the presence of a donor near the centromere: mobility is thus a product of homology identification and increased Rad51-ssDNA filament residency in the vicinity of the centromere, and so downstream of homology search. This is a major pitfall in their interpretation and model.

We thank the referee for helping to clarify the question of the cause and consequence of global mobility. As he pointed out, the fact that a donor is required to observe both H2A phosphorylation and distal mobility implicates the recombination process itself, as well as the residence time of the Rad51 nucleofilament, in the ƴ--‐H2A(X) spreading and indicates that recombination would be the cause of distal mobility. In contrast, the fact that proximal mobility can exist independently of homologous recombination suggests that in this particular configuration, HR would then be a consequence of proximal mobility.

In conclusion, I think the data presented are of importance, as they identify a link between local and global chromatin mobility. The authors should rewrite their manuscript and reorganize the figures to focus on the painter model that their data support. I propose experiments that will help bolster the manuscript conclusions.

1) Attempt dual-color tracking of the DSB (i.e. Rad52-mCherry or Ddc1-mCherry) and the donor site, and track MSD as a function of proximity between the DSB and the Lac array (with DSB +/-dCen). The expectation is that only upon contact (or after getting in close range) should the MSD at the centromere-proximal LacO array increase with a DSB at a subtelomere. Furthermore, this approach will help distinguish MSDs in cells bearing a DSB (Rad52 foci) from undamaged ones (no Rad52 foci)(see Mine-Hattab & Rothstein 2012). This would help overcome the inefficient DSB induction of their system (less than 50% at 1 hr post-galactose addition, and reaching 80% at 6 hr). For the reader to have a better appreciation of the data distribution, replace the whisker plots of MSD at 10 seconds with either scatter dot plot or violin plots, whichever conveys most clearly the distribution of the data: indeed, a bimodal distribution is expected in the current data, with undamaged cells having lower, and damaged cells having higher MSDs.

The reviewer raises two points here.

The first point concerns the residence time of the Rad51 filament with the donor when a subtelomeric DSB happens. Measuring the DSBs as a function of the distance between donor and Rad52mCherry (or Ddc1--‐mCherry) would allow deciding on the cause or the consequence of the global mobility. Thus, if mobility is the consequence of (stochastic) contact, leading to a better efficiency of homologous recombination, we would see an increase in MSDs only when the distance between donor and filament would be small. Conversely, if global mobility is the cause of contact, the increase in mobility would be visible even when the distance between donor and filament is large. It would be necessary to have a labelling system with 3 different fluorophores — the one for the global mobility, the one for the donor and the one allowing following the filament. This triple labelling is still to be developed.

The second point concerns the important question of the heterogeneity of a population, a central challenge in biology. Here we wish to distinguish between undamaged and damaged cells. Even if a selection of the damaged cells had been made, this would not solve entirely the inherent cell to cell variation: at a given time, it is possible that a cell, although damaged, moves little and conversely that a cell moves more, even if not damaged. The question of heterogeneity is therefore important and the subject of intense research that goes beyond the framework of our work (Altschuler and Wu, 2010). However, in order to start to clarify if a bias could exist when considering a mixed population (20% undamaged and 80% damaged), we analyzed MSDs, using a scatter plot. We considered two population of cells where the damage is the best controlled, i.e. i) the red population which we know has been repaired and, importantly, has lost the cut site and will be not cut again (undamaged--‐only population) and ii) the white population, blocked in G2/M, because it is damaged and not repaired (damaged--‐only population). These two populations show very significant differences in their median MSDs. We artificially mixed the MSDs values obtained from these two populations at a rate of 20% of undamaged--‐only cells and 80% of damaged--‐only cells. We observed that the mean MSDs of the damaged--‐only and undamaged--‐only cells were significantly different. Yet, the mean MSD of damaged--‐only cells was not statistically different from the mean MSD from the 20%--‐80% mixed cell population. Thus, the conclusions based on the average MSDs of all cells remain consistent.

Scatter plot showing the MSD at 10 seconds of the damaged-­‐only population (in white), the repaired-­‐only population (in red), or the 20%-­‐80% mixed population

2) Perform the phospho-H2A ChIP-qPCR in the C and S strains in the absence of Rad51 and Rad9, to strengthen the painter model.

ChIP experiments in mutant backgrounds as well as phosphorylation/dephosphorylation kinetics would corroborate the mobility data described here, but are beyond the scope of this manuscript. Yet, a phospho--‐ H2A ChIP experiment was performed in a Δrad51 mutant in Renkawitz et al. 2013. In that case, γH2A propagation was restricted only to the region around the DSB, corroborating both the requirement for Rad51 in distal mobility and the lack of requirement for Rad51 in proximal mobility.

3) Their data at least partly run against previously published results, or fail to account for them. For instance, it is hard to see how their model (or the painter model), could explain the constitutively activated global mobility increase observed by Smith .. Rothstein 2018 in a rad51 rad52 mutant. Furthermore, the gasser lab linked the increased chromatin mobility to a general loss of histones genome-wide, which would be inconsistent with the more localized mechanism proposed here. Do they represent an independent mechanism? These conflicting observations need to be discussed in detail.

Apart from the fact that the mechanisms in place in a haploid or a diploid cell are not necessarily comparable, it is not clear to us that our data are inconsistent with that of Smith et al. (Smith et al., 2018). Indeed, it is not known by which mechanisms the increase in global mobility is constitutively activated in a Δrad51 Δrad52 mutant. But according to their hypothesis the induction of a checkpoint is likely and so is the phosphorylation of H2A. It would be interesting to verify γH2A in such a context. This question is now mentioned in the main text.

Concerning histone loss, it appears to be different depending on the number of DSBs. Upon multiple DNA damage following genotoxic treatment with Zeocin, Susan Gasser's group has clearly established that nucleosome loss occurs (Cheblal et al., 2020; Hauer et al., 2017). Nucleosome loss, like H2A phosphorylation as we have shown (Garcia Fernandez et al., 2021; Herbert et al., 2017), leads to increased global mobility. The state of chromatin following these histone losses or modifications is not yet fully understood, but could coexist. In the case of a single DSB by HO, it is the local mobility of the MAT locus that is examined (Fig3B in (Cheblal et al., 2020). In this case, the increase in mobility is indeed dependent on Arp8 which controls histone degradation and correlates with a polymer pattern consistent with normal chromatin. It is likely that histone degradation occurs locally when a single DSB occurs. Concerning histone loss genome wide, the question remains open. If histone eviction nevertheless occurred globally upon a single DSB, both types of modifications could be possible. This aspect is now mentioned in the discussion.

Author Response:

Reviewer #3 (Public Review):

INaR is related to an alternative inactivation mode of voltage activated sodium channels. It was suggested that an intracellular charged particle blocks the sodium channel alpha subunit from the intracellular space in addition to the canonical fast inactivation pathway. Putative particles revealed were sodium channel beta4 subunit and Fibroblast growth factor 14. However, abolishing the expression of neither protein does eliminate INaR. Therefore as recently suggested by several authors it is conceivable that INaR is not mediated by a particle driven mechanism at all. Instead, these and other proteins might bind to the pore forming alpha subunit and endow it with an alternative inactivation pathway as envisioned in this paper by the authors.

The main experimental findings were (1) The amplitude of INaR is independent of the voltage of the preceding step. (2) The peak amplitudes of INaR are dependent on the time of the depolarizing step but independent of the sodium driving force. (3) INaT and INaR are differential sensitive to recovery from inactivation. According to their experimental data the authors put forward a kinetic scheme that was fitted to their voltage-clamp patch-clamp recordings of freshly isolated Purkinje cells. The kinetic model proposed here has one open state and three inactivated states, two states related to fast inactivation (IF1, IF2) and one state related to a slower process (IS). Notably IS and IF are not linked directly in the kinetic scheme.

In my humble opinion, the proposed kinetic model fails to explain important experimental aspects and falls short to be related to the molecular machinery of sodium channels as outlined below. Still it is due time to advance the concepts of INaR. The new experimental findings of the authors are important in this respect and some ideas of the new model might be integrated in future kinetics schemes. In addition, the framework of INaR is not easy to get hold on with lots of experimental findings in the literature. Likely, my review falls also short in some aspects. Discussion is much needed and appreciated.

INaT & INaR decay The authors stated that decay speed of INaT and INaR is different and hence different mechanisms are involved. However at a given voltage (-45 mV) they have nicely illustrated (Fig. 2D and in the simulation Fig. 3H) that this is not the case. This statement is also not compatible with the used Markov model. That is because (at a given voltage) the decay of both current identities proceed from the same open state. Apparent inactivation time constants might be different, though, due to the transition to the on state.

We apologize that the language used was confusing. Our suggestion that there is more than one pathway for inactivation (from an open/conducting state) is the observation that the decay of INaT being biexponential at steady-state voltages. In the revised manuscript, we point out (lines 546-549) that, at some voltages, the slower of the two decay time constants (of INaT) is identical to the time constant of INaR decay. We also discuss how this observation was previously (Raman and Bean, 2001) interpreted.

Accumulation in the IS state after INaT inactivation in IF1 and IF2 has to proceed through closed states. How is this compatible with current NaV models? The authors have addressed this issue in the discussion. The arguments they have brought forward are not convincing for me since toxins and mutations are grossly impairing channel function.

Thank you for this comment. We would like to point out that, in our Markov model, Nav channels may accumulate in IS through either the closed state or open state. This requires, of course, that Nav channels can recover from inactivation prior to deactivation. While we agree that toxins and mutations can grossly impair channel function, we think these studies remain crucial in revealing the potential gating mechanisms of Nav channel pore-forming subunits, and how these mechanisms may vary across cell types that express different combinations of accessory proteins.

Fast inactivation - parallel inactivation pathways Related to the comment above the motivation to introduce a second fast-inactivated state IF2 is not clear. Using three states for inactivation would imply three inactivation time constants (O->IF1, IF1->IF2, O->IS) which are indeed partially visible in the simulation (Fig. 3). However, experimental data of INaT inactivation seldom require more than one time constant for fast inactivation. Importantly the authors do not provide data on INaT inactivation of the model in Fig. 3. Fast Inactivation is mapped to the binding of the IFM particle. In this model at slightly negative potential IF1 and IF2 reverse from absorbing states to dissipating states. How is this compatible with the IFM mechanism? Additionally, the statements in the discussion are not helpful, either a second time constants is required for IF (two distinct states, with two time constants) or not.

We thank this Reviewer for this comment. We tried to developed the model based on previous data on Nav channel inactivation. Indeed, much experimental data exists for the fast inactivation pathway (O -> IF1). As we noted in the discussion, without the inclusion of the IF2 state, we were unable to fully reproduce our experimental data, which led us to add the IF2 state. As with all model development, we balanced the need to faithfully reproduce the experimental data with efforts to limit the complexity of the model structure. In addition, as noted in the Methods section, our routine is an automatic parameter optimization routine that seeks to minimize the error between simulation and experiments. We can never be sure that we have found an absolute minimum, or that the optimization got stuck at a local minimum when simulating without inclusion of IF2. In other words, there may be a parameter set that sufficiently fits the data without inclusion of IF2, but we were unable to find it. As a safeguard against local minima, we used multistarts of the optimization routine with different initial parameter sets. In each case, we were unable to find a sufficiently acceptable parameter set.

We agree with this Reviewer that at slightly negative potentials (compared to strong depolarizations), channels exit the IF1 state at different rates, although we would point out that channels dissipate from the IF1 state (accumulating into IS1) under both conditions (see Figure 8B-C). This requires the binding and unbinding of the IFM motif to occur with some voltagesensitivity. We believe this to be a possibility in light of evidence that suggests IFM binding (and fast-inactivation) is an allosteric effect (Yan et al., 2017) and evidence showing that mutations in the pore-lining S6 segments can give rise to shifts of the voltage-dependence of fast inactivation without correlated shifts in the voltage-dependence of activation (Cervenka et al., 2018). However, it remains unclear how voltage-sensing in the Nav channel interact with fast- and slow-inactivation processes.

Due to space constraints in Figure 3, we did not show a plot of INaT voltage dependence. However, below, please find the experimental data (points), and simulated (line) INaT in our model.

Differential recovery of INaT & INaR Different kinetics for INaR and INaR are a very interesting finding. In my opinion, this data is not compatible with the proposed Markov model (and the authors do not provide data on the simulation). If INaT1 and INaT2 (Fig. 5 A) have the same amplitude the occupancy of the open state must be the same. I think there is no way to proceed differentially to the open state of INaR in subsequent steps unless e.g. slow inactivated states are introduced.

Thank you for bringing up this important point. The differential recovery of INaT and INaR indicates there are distinct Nav channel populations underlying the Nav currents in Purkinje neurons. We make this point on lines 632-635 of the revised manuscript. Because our Markov model is used to simulate a single channel population, we do not expect the model to reproduce the results shown in Figure 5. We have now added this point to the Discussion section on lines 637-640.

Kinetic scheme Comparison with the Raman-Bean model is a bit unfair unless the parameters are fitted to the same dataset used in this study. However, the authors have an important point in stating that this model could not reproduce all aspects of INaR. A more detailed discussion (and maybe analysis) of the states required for the models would be ideal including recent literature (e.g., J Physiol. 2020 Jan;598(2):381-40). Could the Raman-Bean model perform better if an additional inactivated state is introduced? Are alternative connections possible in the proposed model? How ambiguous is the model? Is given my statements above a second open state required? Finally, a better link of the introduced states to NaV structure-function relationship would be beneficial.

These are all excellent points. We absolutely agree; it was/is not our intention to “prove” that the Raman-Bean model does not fit our dataset (as you mention, with proper refinement of the parameters, some of the data may be well fit). In fact, qualitatively we found the Raman-Bean model quite consistent with our dataset (which is an excellent validation of both the model, and our data). It was our intention to show (in Figure 7) that there is good agreement between the Raman-Bean model and our experimental data for steady state inactivation (C), availability (D), and recovery from inactivation (E). While we find the magnitude of the resurgent current (F) to be markedly different than the Raman-Bean data, we now note this to likely be due to the large differences in the extracellular Na+ concentrations used in voltage-clamp experiments (lines 440-444). Our models, however, specifically differ in our parallel fast and slow inactivation pathways (Figure 7H). As seen in the Raman-Bean model, in response to a prolonged depolarizing holding potential, there is negligible inactivation, as the OB state remains absorbent until the channel is repolarized. This is primarily because the channel must transit through the Open state on repolarization. We find distinctly different behavior in our data. As seen in the experimental data shown in 7H, despite a prolonged depolarization, Nav channels begin to inactivate and accumulate in the slow inactivated state without prerequisite channel opening. This behavior is impossible to fit in the Raman-Bean model, given the topological constraint of the model requiring a single pathway through the open state from the OB state.

To that point, it is also unlikely that the addition of inactivated states to the Raman-Bean model would help fit this new dataset. Indeed, the Raman-Bean model contains 7 inactivated states. If there were a connection between OB ->I6, it is possible that direct inactivation (bypassing the O state) may help. Again, however, it is not our intention to discredit the Raman-Bean model, nor is it our intention to improve the Raman-Bean model. With new datasets, a fresh look at model topology was undertaken, which is how we developed our proposed model.

This Reviewer astutely points out a known limitation of Markov (state-chain) modeling; it is impossible to tell uniqueness, or ambiguity of the model (both with parameters as well as model topology). Following the results of Menon et al. 2009 (PNAS vol. 106 / #39 / 16829 – 16834), in which they used a state mutating genetic algorithm to vary topologies of a Markov model, our group (Mangold et al. 2021, PLoS Comp Bio) recently published an algorithm to distinctly enumerate all possible model structures using rooted graph theory (e.g. all possible combinations of models, rooted around a single open state). What we found (which is not entirely surprising) is that there are many model structures and parameter sets that adequately fit certain datasets (e.g., cardiac Nav channels).

Therefore, the goal is never to find the model (indeed we don’t propose that we have done so), but rather to find a model with acceptable fits to the data and then use that model to hypothesize why that model structure works, as well as to hypothesize higher dimensional dynamics. We make these points in the revised manuscript (lines 591-597).

We did not specifically explore the impact of a second open state in our modeling and simulation studies, but we would certainly agree that a model with a second open state may recapitulate the dataset.

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):

"Modality-specific tracking of attention and sensory statistics in the human electrophysiological spectral exponent," Waschke et al. This paper follows upon a recent paper by a subset of the same authors that laid out the signal processing-bases for decomposing the EEG signal into periodic (i.e., "oscillatory") and aperiodic components (Donoghue et al., 2020). Here, the focus is on establishing physiological and functional interpretations of one of these aperiodic components: the exponent term of the 1/f(to the x power) fit to the power spectrum (a.k.a., its 'slope'). This is very important work that will have strong and lasting impact on how people design and interpret the results from EEG experiments, and is also likely to trigger many reanalyses of previously published data sets. However, the manuscript could do a better job of explain WHY this is so. In this reviewer's opinion, more linkage with elements of Donoghue et al. (2020). would help considerably.

First, a brief summary of what this manuscript does, and why it is important. The first section reanalyzes data sets in human subjects undergoing ketamine or propofol anaesthesia, known to influence the E:I balance in the neural circuits that give rise to the EEG. This is an important step in establishing the physiological validity of the fundamental proposition that flattening of the 1/f component reflects an increase in the E:I balance whereas steepening reflects a decrease. This is because these effects of these two anaesthetic agents has been well established in several invasive studies. The second section demonstrates the functional properties of 1/f slope, in that tracks shifts of attention between visual and auditory stimuli in an electrode-specific manner (i.e., posterior for visual, central for auditory), and it also captures aperiodic stucture in these stimuli. It's not too strong to say that, after this paper, EEG-related research will never be the same again. The reason for this, however, isn't stated as clearly as it could be.

Thank you for your positive appraisal of our work! We appreciate that you see significant benefit to this work, and also understand that you see significant room from improvements in the way results are presented, framed and discussed and want to express our thanks for these helpful comments. Below, we elaborate on them and the changes they prompted in greater detail.

With regard to exposition, the manuscript could be improved in terms of building on Donoghue et al. (2020). To simplify, a main take-away from Donoghue et al. (2020) is that many past interpretations of EEG signals have mistakenly attributed to task- (or state-) related changes to changes in one or more oscillatory components of the signal. Perhaps most egregiously, what can appear as a change in power in the alpha band can often be shown to be better explained as no change in alpha but instead a change in either the slope or the offset of the 1/f component of the power spectrum. (E.g., the bump at 10 Hz will increase or decrease if the slope of the 1/f component changes, even though the 'true' oscillator centered at 10 Hz hasn't changed.) In this paper, the authors demonstrate that many conditions, physiological state and cognitive challenge, influence 1/f slope in ways that are systematic and that occur independent of changes that may or may not be occuring simultaneously in oscillatory alpha. Broadly, the authors should consider two modifications: first, point out for each key experimental finding how attributing everything to changes in oscillatory alpha (or sometimes other frequencies) would lead to flawed inference; second, don't stop at demonstrating that the slope effects hold when alpha dynamics are partialed out, but also report the converse -- in what ways is oscillatory alpha sensitive to aspects of physiology and/or behavior that 1/f slope is not? Even if there aren't any such cases (which seems unlikely) it would be informative for this to be tested and reported.

We agree that a stronger focus on the differentiation between oscillatory and 1/f aspects of EEG activity can help to improve the didactic strength of our manuscript. Wherever possible, we have tried to make clear that the separation of different oscillatory activity and aperiodic signals is essential to not confuse one for the other. This is not only the case for the analysis of anaesthesia data were changes in alpha and beta power have to be separated from changes in spectral exponent but also applies to the proposed attention contrast where common effects of alpha power have to be taken into account and differentiated from spectral exponents. Similarly, an alignment of stimulus spectra with EEG activity could appear as a twofold power change (e.g., increase over low, decrease over high frequencies) if no separation of oscillatory and aperiodic signal parts is performed.

We agree that explicitly contrasting spectral exponents with estimates of low-frequency or alpha power is essential. The original version of the manuscript already included such a comparison for the effect of attention on EEG spectral exponents and alpha power, respectively. To expand this approach, we inverted models and used stimulus spectral exponents (auditory or visual) as dependent variables while using either EEG spectral exponents, low-frequency power or alpha power as predictors (among the same covariates as in the winning models of the original approach). In a next step, we used likelihood ratio tests to compare model fit separately at each electrode, resulting in a topography of model comparisons.

(a) Attention contrasts

As expected, based on decades of EEG research, and as can be seen in figure 3C, average EEG alpha power changed as a function of attentional focus, in a topographically specific manner. Importantly, the observed increase of alpha power from auditory to visual attention took place over and above the reported changes in EEG spectral exponents (as we had reported in the control analyses section). In other words, both EEG spectral exponents and EEG alpha power capture attention-related changes in brain dynamics, but are at least partially sensitive to distinct sources or mechanisms. In the updated version of the manuscript, we emphasize that changes in spectral exponents often can be mistaken for changes in alpha power (as in Donoghue et al., 2020), calling for a dedicated spectral parameterization approach. Attention-related changes in spectral exponents and alpha power might depict results of distinct modes of thalamic activity that transitions from tonic to bursty firing and shapes cortical activity to selectively process attended sensory input. In the updated version of the manuscript, we discuss the potential role of thalamic activity in greater detail. The updated parts of the discussion section are pasted below for convenience.

“Despite these differences in the sensitivity of EEG signals, our results provide clear evidence for a modality-specific flattening of EEG spectra through the selective allocation of attentional resources. This attention allocation likely surfaces as subtle changes in E:I balance (Borgers et al., 2005; Harris and Thiele, 2011). Importantly, these results cannot be explained by observed attention-dependent differences in neural alpha power (8–12 Hz, Fig 3) which have been suggested to capture cortical inhibition or idling states (Cooper et al., 2003; Pfurtscheller et al., 1996). Also note that the employed spectral parameterization approach enabled to us to separate 1/f like signals from oscillatory activity and hence offered distinct estimates of spectral exponent and alpha power that would otherwise have been conflated (Donoghue et al., 2020).

How could attentional goals come to shape spectral exponents and alpha oscillations? Both attention-related changes in EEG activity might trace back to distinct functions of thalamo-cortical circuits. On the one hand, bursts of thalamic activity that project towards sensory cortical areas might sculpt cortical excitability in an attention-dependent manner by inhibiting irrelevant distracting information (Klimesch et al., 2007; Saalmann and Kastner, 2011). On the other hand, tonic thalamic activity likely drives cortical desynchronization via glutamatergic projections and, with attentional focus, results in boosted representations of stimulus information within brain signals (Cohen and Maunsell, 2011; Harris and Thiele, 2011; Sherman, 2001).

Our findings of separate attentional modulations of both, EEG spectral exponents and alpha power, point towards the involvement of both thalamic modes in the realization of attentional states. Recently, momentary trade-offs between both modes of thalamic activity have been suggested to give way to attention-related modulations of alpha power and E:I balance, as captured by EEG spectral exponents (Kosciessa et al., 2021). Here, task difficulty remained constant throughout the experiment an fluctuations between both modes might not follow momentary demand (Kosciessa et al., 2021; Pettine et al., 2021) but varying sensory-cognitive resources.

Additionally, modulations of both alpha power and EEG spectral exponents appeared uncorrelated across individuals - further evidence that they reflect separate neural sources. Future studies that combine a systemic manipulation of E:I (e.g., through GABAergic agonists) with the investigation of attentional load in humans are needed to specify with greater detail how thalamic activity modes drive alpha oscillations and EEG spectral exponents. Specifying potential demand- and resource-dependent trade-offs between different modes of attention-related modulations of cortical activity and sensory processing will offer crucial insights into the neural basis of adaptive behaviour.”

(b) Stimulus spectral exponent tracking

We inverted all models and instead of modelling EEG spectral exponents, we used auditory or visual stimulus exponents as dependent variables. Predictors were identical to the previously reported models (see supplementary table for all details) but additionally included either single trial estimates of alpha power, low-frequency power, or EEG spectral exponents. Note that alpha power estimates were extracted using the same spectral parameterization approach that was used to estimate spectral exponents. Trials without an oscillation in the alpha range were excluded from all models to render likelihood comparisons interpretable (11.2%  3.4 %). Since oscillations were only seldomly detected in the low-frequency range (1–5 Hz), we instead used single trial power averaged across this range. For each electrode, 4 likelihood ratio tests were performed, one for each stimulus modality and one for each predictor (low-frequency or alpha power). Strikingly, low-frequency power resulted in worse model fits (non-positive likelihood ratio test statistics) compared to EEG spectral exponents across all electrodes and both stimulus modalities. The same was true for EEG alpha power when modelling auditory stimulus exponents. However, when modelling visual stimulus exponents, EEG alpha power displayed significantly improved model fit at one parietal electrode. In line with this observation, we observed a positive relationship between single trial alpha power and visual stimulus exponents at this parietal site (see below).

Figure R5 Model comparison topographies. (a) Single trial auditory (upper row) or visual stimulus exponents (lower row) were modelled based on electrode wise low frequency power (left column) or alpha power (right) column, among other covariates. Models were compare d to a model of same size that only differed in the main predictor that consisted of single trial EEG spectral exponents. Topographies display the likelihood ratio test statistic, illustrating no improvements in model fit compared to EEG spectral exponent based models in all but one model family, illustrating the unique predictive power of aperiodic EEG activity in this context. Alpha power at one parietal electrode explained significantly more variance in visual stimulus exponents. (b) T values representi ng the main effect of alpha power on visual stimulus exponents. Highlighted electrode represents p< .05 after FDR correction.

(c) Behavioural relevance of spectral exponent tracking

Given the results from (b), we refrained from re-running PLS analysis focussing on the behavioural relevance of the links between low-frequency and alpha power with stimulus exponents. In our view, the absence of a significant link between single trial stimulus input and a measure of neural activity in this case precludes any further analysis on the between-subject level.

Reviewer #2 (Public Review):

The paper investigates two separate studies looking at the spectral exponent of the EEG 1/f-like spectrum: one a study of the effect of anesthesia type (propofol vs. ketamine), using publicly available data, and the other a traditional study of auditory and visual processing relying on selective attention to one modality vs. the other. The authors make a strong case that the value of the spectral exponent depends on the relevant condition, in both studies, but the case for the spectral exponent's dependence on the Excitation:Inhibition balance is much weaker.

The paper presents the two separate studies as tightly linked, but by the end of the paper it appears they may be quite separate.

The anesthesia study is brief and compelling. With respect to the effect of anesthesia type on spectral exponent, the results are very strong, and, given the results of Gao et al. (2017) and the stated properties of propofol vs. ketamine, the connection to E:I balance follows naturally.

The auditory and spectral 1/f tracking study suffers from some weaknesses.

Most importantly, the design is elegant and the results presented are very compelling. 1) Modality-specific attention selectively reduces the EEG spectral exponent (for relevant electrodes reflecting cortical processing of that modality); 2) Changing the value of the spectral exponent in the stimulus results in a similar change in the value of the spectral exponent of the response, but only for the selectively attended modality (and only for relevant electrodes); and 3) the amount of modality-specific spectral-exponent tracking predicts behavior. The interactions and main effects found all support the importance of the spectral exponent as a physiologically and behaviorally important index.

The main problem is a weakness in analysis regarding whether the mechanistic origin of the above effects may be due to temporal tracking of the stimulus waveform (visual contrast/acoustic envelope) by the response waveform. [In the speech literature this would be referred to as "speech tracking", or, sometimes, as speech entrainment (in the weak sense of "entrainment").] As pointed out by the authors, this is not a steady state response because the instantaneous fluctuation rate of the stimulus is constantly changing, and so cannot be analyzed as such (it is also distinct from the evoked responses analyzed). But it is a good match for other analysis methods, for instance Ed Lalor's VESPA and AESPA methods, and their reverse-correlation descendants. Specifically, Lalor et al., 2009 analyzed EEG responses to a non-sinusoidal envelope modulation of a broadband noise carrier and found strong evidence for robust temporal locking. The success of such linear methods there (AESPA for auditory; VESPA for visual) implies that a change in the stimulus spectrum exponent would produce a similar change in the response spectrum exponent, having nothing to do with E:I balance.

The evoked response analysis clearly aims to go in this direction, but since it does not reflect ongoing response properties, it cannot alone speak to this.

Because this plausible mechanism for the spectral-exponent-tracking has not been explored, it is much harder to associate the observed spectral-exponent-tracking as originating from E:I balance. The study does not then hold together well with the anesthesia study, and weakens the links to E:I balance rather than strengthening it.

Thank you for this in-depth assessment of our work and your general positive appraisal of it. Importantly, your major point of concern seems to at least partially trace back to a regrettable misunderstanding caused by the way we presented our results in the original version of the manuscript. While the first study aimed at establishing the validity of the EEG spectral exponent as a non-invasive marker of E:I, the second study had two objectives. First, to test attention-related changes in EEG spectral exponents that we assume to depict topographically specific changes in E:I. Second, to test the link between aperiodic stimulus features and aperiodic EEG activity by comparing stimulus spectral exponents and EEG spectral exponents. We understand that the reviewer is doubtful of the link between stimulus-related EEG spectral exponent changes and E:I – and so are we.

In the updated version of the manuscript, we have tried to make it very clear that despite the displayed and inferred links between EEG spectral exponents and E:I balance, the positive relationship between stimulus spectral exponents and EEG spectral exponents does not necessarily reflect changes in E:I. Nevertheless, we feel that study 1 and 2 integrate well as they offer a comprehensive view on 1/f-like EEG activity and its sensitivity to (1) specific anaesthesia effects, (2) attentional focus, and (3) aperiodic stimulus features in a behaviourally-relevant way. While (1) and (2) can be mapped on to one underlying mechanism, cortical E:I balance, (3) rather represents bottom-up sensory cortical effects similar to those described in SSEP or speech tracking literature. The interaction of attentional focus and stimulus tracking illustrates the connection between top-down (or anaesthesia-driven) changes in E:I as captured by the EEG spectral exponent, and bottom-up sensory-related changes in EEG activity.

Reviewer #3 (Public Review):

The balance between excitation and inhibition in the cortex is an interesting topic, and it has already been a focus of study for a while. The current manuscript focuses on the 1/f slope of the EEG spectra as the neural substrate of the change in the balance between excitation and inhibition. While the approach they use to analyze their data is interesting, unfortunately, for the reasons I'll outline below the study's conclusions are not supported by the data, and the findings do not add any new insight conceptually or mechanistically to our understanding of attention, excitation or inhibition. While the study aims to "test the conjecture that 1/f-like EEG activity captures changes in the E:I balance of underlying neural populations.", ultimately the central conclusions of the work is just conjecture in that they are inference formed without sufficient evidence.

Anaesthesia study: EEG spectral exponents as a non-invasive approximation of E:I balance The authors observe the 1/f slope was different over pre-selected central electrodes sites between 4 participants undergoing ketamine and propofol anaesthesia. The rather small sample size is a cause for concern, as are the authors' rationale for looking at the central electrodes -they claim these electrodes receive contributions from many cortical and subcortical sources, but that can be said of any other electrodes at the scalp. But I believe the most critical weakness here is the authors' claim that during anaesthesia is that propofol is "known" to result in a "net" increase of inhibition, while ketamine an increase in net excitation. We still know very little about what neurophysiologically is happening under anaesthesia and the concept of "net" inhibition and excitation is rather a gross simplification of what happens to the central nervous system under these two agents. Just as an example, propofol has been found to have some excitatory influence on brain function, with dosage of the anaesthetic also playing role: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC2717965/. On the other hand, ketamine has been observed to inhibit interneurons and cortical stimulus-locked responses, but cause excitation in the auditory cortex : https://physoc.onlinelibrary.wiley.com/doi/10.1113/JP279705.

Suffice to say the interaction between anaesthetic agents and the brain is rather complex. Decades of research has shown that the EEG spectra changes during anaesthesia. To rather arbitrarily say one agent has a net inhibitory impact while another excitatory impact, then link those to qualitative changes in the EEG spectra of 4 participants, and further link that back to E:I ratio is committing the scientific fallacy of Begging the Claim.

We thank the reviewer for their insightful comments. Of course, we do not wish to challenge the complex nature of anaesthetic effects by any means and apologize if the original version of our manuscript had left that impression. Below, we outline that despite the complex impact of anaesthesia on central nervous activity, there exists plenty of evidence justifying our assumption of differentially altered E:I balance through propofol and ketamine, at least in cortical areas.

First of all, we agree with the reviewer that a change in E:I balance certainly is not the only change that takes place in the central nervous system during anaesthesia. As has been shown before, propofol and ketamine affect the overall level of neural activity (Taub et al., 2013) and spiking (Quirk et al., 2209; Kajiwara et al., 2020), propofol is associated with frontal alpha oscillations and widespread changes in beta power (Purdon et al., 2012). In the updated version of the manuscript, we have added notions to these common patterns and discuss the oscillatory changes we observe in the current dataset.

Importantly, while there might not be a single identifiable mechanism behind the host of different anaesthesia-induced changes in brain activity, there is relative clarity on the fact that higher doses of propofol drive a change in excitatory and inhibitory activity towards inhibition whereas ketamine drives disinhibition and hence shifts E:I towards excitation. In fact, the study by Deane et al. (2020) reports increased excitation and disinhibition in auditory cortex during ketamine anaesthesia, accompanied by stronger (not weaker, as stated by the reviewer) evoked responses. These findings speak to the validity of the simplification of a net increase of excitation under ketamine anaesthesia. Furthermore, the modelling results by McCarthy et al. (2008) target a dose- and cell-ensemble specific effect of propofol anaesthesia: paradoxical excitation. The observation that low doses of propofol can induce a temporary increase of excitatory activity is in stark contrast to the general GABA-A-potentiating and hence inhibiting nature of propofol (Concas et al., 1991). Importantly, however, higher doses of propofol as used in the analysed dataset are widely accepted to lead to relatively increased inhibition, even after initial paradoxical excitation (Concas et al., 1991; Zhang et al., 2009; Brown et al., 2011; Ching et al., 2010). Taken together, previous invasive physiology justifies the simplification of propofol as leading to net increased inhibition and ketamine leading to net excitation. Finally, our focus on the spectral exponent does not stem from a disregard of oscillatory changes in EEG activity but rather strictly follows from previous work that demonstrated the spectral exponent as a marker of E:I balance (Gao et al., 2017; Colombo et al., 2020; Lendner et al., 2021; Chini et al., 2021). Hence, the central goal of the presented analyses and results lies in the transfer of these previous results to non-invasive EEG recordings and the parameterization approach used by us. We hope that this becomes clearer in the updated version of the manuscript and have pasted relevant parts below.

“Both anaesthetics exert widespread effects on the overall level of neural activity (Taub et al., 2013) as well as on oscillatory activity in the range of alpha and beta (8–12 Hz; ~15–30 Hz). Importantly, however, propofol is known to commonly result in a net increase of inhibition (Concas et al., 1991; Franks, 2008) whereas ketamine results in a relative increase of excitation (Deane et al., 2020; Miller et al., 2016). In accordance with invasive work and single cell modelling (Chini et al., 2021; Gao et al., 2017), propofol anaesthesia should thus lead to an increase in the spectral exponent (steepening of the spectrum) and ketamine anaesthesia to a decrease (flattening). Based on previous results, the effect of anaesthesia on EEG spectral exponents is expected to be highly consistent and display little topographical variation (Lendner et al., 2020). For simplicity, we focused on a set of 5 central electrodes that receive contributions from many cortical and subcortical sources (see Fig 1) but report topographically-resolved effects in the supplements (see Fig 1 supplement 1). Here, propofol anaesthesia led to an overall increase in EEG power which was especially pronounced in the alpha-beta range. Ketamine anaesthesia decreased the frequency of alpha oscillations and supressed power in the beta range. Importantly, however, EEG spectral exponents that were estimated while accounting for changes in oscillatory activity increased under propofol and decreased under ketamine anaesthesia in all participants (both ppermuted < .0009, Fig 1). These results replicate previous invasive findings and support the validity of EEG spectral exponents as markers of overall E:I balance in humans.”

“[…] While the EEG spectral exponent as a remote, summary measure of brain electric activity can obviously not quantify local E:I in a given neural population, the non-invasive approximation demonstrated here enables inferences on global neural processes previously only accessible in animals and using invasive methods. Future studies should use a larger sample to directly compare dose-response relationships between GABA-A agonists or antagonists (e.g., Flumanezil) and the EEG spectral exponent as well as common oscillatory changes.”

Regarding the reviewer’s comment on our choice of electrodes we first wish to highlight that several previous studies have revealed that anaesthesia effects commonly appear throughout the cortex of humans (Zhang et al., 2009; Lendner et al., 2020). Nevertheless, we understand that a priori choices of electrodes always are arbitrary to some degree. Hence, we performed pairwise comparisons of EEG spectral exponents between awake rest and anaesthesia (ketamine vs. propofol) at all 60 electrodes, resulting in the topographies of t-values shown below. As can be discerned from these topographies, ketamine anaesthesia entailed a reduction of spectral exponents across most areas of the scalp, peaking at frontal and central sites. Propofol led to increased EEG spectral components across all electrodes without a clear spatial pattern. The absence of an effect at the left mastoid likely traces back to artefactual recordings at that electrode site. In the updated version of the manuscript, we report topographies of comparisons in the supplements (figure 1 supplement 2).

Figure R8 Topographically resolved t statistics comparing EEG spectral exponents between awake rest and different anaesthetics. Propofol leads to a wide spread increase in spectral exponents that is present across the entire scalp (left). Ketamine leads to a reduction in spectral exponents that is widely distributed but appears to peak at frontal and central electrodes (right).

We acknowledge the small sample size of study 1 and have also added a more explicit notion to that in the updated version of our manuscript. Nevertheless, due to their consistency and the used permutation-based statistics which are appropriate for small sample sizes, the results of study can be interpreted. Furthermore, we realized that we had not included two additional participants of the publicly available dataset in our previous analysis. Both sets of recordings (ketamine / propofol) were included in the revised analyses of the data, further strengthening the reported results. Hence, despite the small sample size (now N = 5 per group), we believe that the used methods and the consistency of effects allows for a careful but clear interpretation, especially since they are in close agreement with previous invasive and modelling results as well as recent causal manipulation studies (Gao et al., 2017; Chini et al., 2021).

Cross-modal study: EEG spectral exponents track modality-specific, attention-induced changes in E:I Here the authors observe a difference in 1/f slope depending on if the participants (n=24) were paying attention to the auditory or visual stream. My central issue here is again with the authors' assumptions: cross-modal attention reflects attention-induced E/I. While attention to a single sensory modality can result in decreased activity in cortical regions that process information from an unattended sensory modality, there is no basis here to say that the task-irrelevant region is actually inhibited. The authors here do observe differences in 1/f slope as a function of attentional location, and these differences do account for some of the variances in behavior in the task.

But unfortunately other than a purely descriptive exercise, there is not any sort of mechanistic insight is revealed here with regards to attentional allocation, excitation, and inhibition.

We wish to take this opportunity to briefly elaborate on our hypotheses behind the reported attention contrasts and their interpretation. Spectral exponents of invasively recorded neural field potentials have previously been shown to reflect pronounced changes in E:I balance, including recent causal optogenetic work explicitly testing this link (Gao et al., 2017; Chini, Pfeffer & Haganu-Opatz 2021). In a first step, we analysed data from different anaesthetics to establish the potency of non-invasive EEG recordings to track similar changes (see above). Building on these findings, we tested whether smaller, attention-related and topographically-specific changes in E:I balance can equally be observed by means of EEG spectral exponent changes. Importantly, topographically concise changes in E:I with attention have been reported previously in non-human animals (e.g., Kanashiro et al., 2017; Ni et al., 2018). We found an attention-related topographical pattern of EEG spectral exponents in support of such an idea: spectral exponents at occipital channels decreased during visual attention, pointing towards a relative increase of excitatory activity in visual cortical areas. The same effect was reduced at central electrodes and for auditory attention. These findings demonstrate the potency EEG spectral exponents to detect topographically-specific attention-related changes in brain activity that likely trace back to changes in E:I balance. Of note, we do not imply a role of E:I in the inhibition of unattended sensory input and activity in associated cortical areas but rather point to a potentially separate role of neural alpha power in this context. While it is generally difficult to draw strictly mechanistic insights based on correlational designs, our results at least strongly suggest a mechanistic role of modality-specific attention for EEG dynamics and E:I balance. Furthermore, by demonstrating separate effects of aperiodic activity and alpha power dynamics, we pave the way for a new line of studies (see comments by R1) on the neural dynamics of selective attention and their behavioural relevance in humans.

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):

The tools and approaches in this manuscript are of broad interest, not only to protein engineers but also to the many researchers using genome-editing reagents. However, putting the work in the context of previous research, both through changing the writing and additional experiments, will be critical for taking advantage of that widespread applicability.

Strengths:

Overall, the data support the conclusions of the manuscript.

The most exciting product of this work is an engineered nuclease, Nsp2-SmuCas9, that has high activity and specificity in human cells and a relaxed PAM preference for a single C base. This chimeric enzyme can efficiently induce indels at endogenous sites. While other works have presented nucleases with minimal PAM preferences, Nsp2-SmuCas9 is a useful alternative and may be preferred. It is also more compact than the standard SpCas9, making it appealing for gene therapy applications.

Technologically, the presented approach of screening orthologs for new specificities and making chimeras to achieve further diversity is a good way to develop new genome-editing reagents. The authors used appropriate methods, such as GUIDE-seq, to complete their goals. Extending beyond the GFP-activation assay to determine activity at endogenous targets enhanced the value of the results.

Conceptually, it was important information to the field that proteins with very high sequence identity (93%) can have divergent PAM preferences. Through their engineering, the authors clearly demonstrate the advantage of characterizing such close orthologs with diverse amino acids in the area of PAM recognition.

Weaknesses:

1) An overall weakness with the work is that it is not clear how the activity level of the relaxed PAM enzyme, Nsp2-SmuCas9, compares to existing enzymes. Is it much better than the SpCas9 that has almost no PAM preference (SpRY) or the NGN PAM (SpG)? How does it compare to the most commonly used SpCas9 nuclease, which is known to be active in a wide variety of biological contexts? The activity assessment at endogenous sites seemed to have a long timeline, as the indel rate was measured 5 days after transfection. Clarifying the effectiveness of this new nuclease would increase the impact of this work.

We sincerely thank the reviewer for the constructive comments on our manuscript. Following reviewer’s suggestions, we compared the editing efficiency of Nsp2Cas9, Nsp2-SmuCas9, SpCas9, SpCas9-NG, and SpCas9-RY side-by-side. Overall, the editing efficiency was low this time probably due to low transfection efficiency. The results revealed that SpCas9 was the most active enzyme. Nsp2Cas9, SpCas9-NG, and SpCas9-RY displayed similar activity. Nsp2-SmuCas9 displayed lower activities than other Cas9 variants (Figure 5C).

2) In the presentation of the manuscript, there are several weaknesses. First, while it is true that allele-specific disruption is an important application of new CRISPR proteins, there are many other reasons why they would be useful. The specific focus on this single application throughout the abstract, introduction and discussion takes away from the widespread utility of these new tools. The writing would be more compelling if it targeted a broader audience. Allele-specific targeting is also possible beyond the PAM site if the mutation is in a position with high specificity.

Many thanks for the reviewer’s suggestions. Following reviewer’s suggestions, we emphasize the widespread utility of these new tools throughout the abstract, introduction, and discussion in the revised manuscript. Allele-specific targeting is only mentioned in the discussion.

3) Second, the introduction is further missing a discussion of other research engineering new PAM specificity or even completely removing specificity. A more convincing narrative would include reasoning for why characterizing naturally occurring orthologs is a powerful and important approach. This information is in the discussion, but it would be helpful for the reader if these points were in the introduction.

Many thanks for the reviewer’s comments. Following reviewer’s suggestions, we added other research engineering new PAM specificity in the introduction. We also included reasoning for why characterizing naturally occurring orthologs is a powerful and important approach.

“Engineered Cas9 variants with flexible PAMs can increase targeting scope. For example, SaCas9 was engineered to accept an NNNRRT PAM [1]; SpCas9 was engineered to accept almost all PAMs [2], but this strategy is time-consuming, and often comes at a cost of reduced on-target activity. Another strategy is to harness natural Cas9 nucleases for genome editing. We have developed several closely related Cas9 orthologs for genome editing [3, 4]. The advantage of developing tools from closely related Cas9 orthologs is that they can exchange the PAM-interacting (PI) domain. If an ortholog recognizes a particular PAM but does not work efficiently in human cells, we can use this ortholog PI to replace another ortholog PI to generate a chimeric Cas9.”

4) A second concern with the presentation and analysis of the findings is a minimal connection to the structural context of the discoveries. Many readers will likely be interested in how the specificity shifts are occurring in these orthologs, which could be remedied by supplementary figures of homology models.

We totally agree with the referee that structural models would help readers better understand the specificity shifts occurring in these orthologs. We have generated calculated structural models of these orthologs in complex with sgRNA and DNA using the crystal structure of Nme1Cas9 (PDB ID: 6JDV). Some specificity shifts can be well explained by these structural models. When the amino acid near the 5 position of the PAM is histidine, its side chain forms a potential hydrogen bond with the 6-hydroxyl group of guanine. Replacement of this guanine by cytosine or thymine would cause a major clash, whereas adenine lacks the hydroxyl group to form hydrogen bond with the histidine (Figure 2-figure supplement 2A). Likewise, an aspartate at 5 position of the PAM would favor a specific recognition of cytosine via hydrogen bonding with its 4-amine group, but not of other bases that may either result in major clash or abolish the hydrogen bond (Figure 2-figure supplement 2B). Similar explanation applies also to the apparent specificity between glutamine and adenine at the 8 position of the PAM on the target sequence (Figure 2-figure supplement 2C).

5) Along the same lines, further structural analysis of the failures would be helpful for those embarking on similar projects. Are there any differences in the sequence or structure of the 4/29 orthologs that were not functional in the GFP-activation assay compared to those that were?

Sequence alignment indicates that the four inactive orthologs possess intact active sites. In the predicted structural models of these orthologs, we did not observe local conformational variations that preclude the interaction with sgRNA or DNA. Sequence alignment indicates that the four inactive orthologs possess intact active sites. In the predicted structural models of these orthologs, we did not observe local conformational variations that preclude the interaction with sgRNA or DNA. We speculate that specific modifications of Cas9s in mammalian cells may occur, leading to the loss of enzymatic activities of the 4 orthologs.

Calculated structural models of AseCas9, Hpa1Cas9, MspCas9, and PlaCas9. Overall calculated structures of AseCas9, Hpa1Cas9, MspCas9, and PlaCas9 with sgRNA and dsDNA.

6) Similarly, it was surprising that the Nsp2-NarCas9 chimera was not active, and it would be helpful if the authors could speculate based on the differences between SmuCas9 and NarCas9, such as at the interface of the domains that were fused. Structural models of the fusions would help the reader to visualize the strategy. Exploring the failures and challenges is important for understanding the generalizability of the presented approach.

Following reviewer’s comments, we generated structural models of Nsp2-NarCas9, Nsp2-SmuCas9, and NarCas9 using the crystal structure of highly homologous Nme1Cas9 in complex with sgRNA and dsDNA (PDB ID: 6JDV) as the template by SWISS-MODEL. By superimposing these models, we noticed that residues G1035, K1037 and T1038 of Nsp2-NarCas9 chimera protrude towards the DNA molecule, which would prevent the binding with DNA and thereby abolishing the editing activity (Figure 4-figure supplement 2A). In comparison, Nsp2-SmuCas9 and NarCas9, which possess the Cas activity, show no protrusion at the corresponding position (Figure 4-figure supplement 2B-C).

7) Finally, the final sequence of Nsp2-SmuCas9 fusion, as well as other enzymes such as the failed Nsp2-NarCas9, are not obvious in the manuscript. I may have missed them, but I also did not see the primers used in the Methods section. Addgene submission is also encouraged and would be of great value to the scientific community.

Thank you for your suggestions. The final sequence of Nsp2-SmuCas9, as well as other enzymes, have been provided in Supplemental file 1. The primers for chimera proteins were listed in Supplemental file 1. We will submit plasmids to Addgene soon.

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):

Most work on antibiotic resistance focuses on particular resistance genes often located on plasmids, but rarely how these genes interact with others located on the chromosome of the host organism. Considering variation in the host genome and its interaction with resistance plasmids can help predict which hosts are more likely to become resistant to a given antibiotic and explain why the same plasmid may not confer the same level of resistance to different strains.

The authors take a clever approach to finding such genetic interactions by designing an evolution experiment using E. coli carrying an MCR-1 plasmid containing resistance genes to colistin. They then select for increased resistance to colistin and sequence the genomes of the most resistant isolates. This allowed them to identify a particular gene lpxC that confers increased resistance to E. coli when combined with the MCR-1 plasmid (more than the sum of each mutation alone) and find that this is because of decreased membrane surface charge. They then investigate whether this mutation is relevant in wild E. coli isolates by analysing environmental samples from patients and other sources and find that indeed, this mutation is often found in carriers of the MCR-1 plasmid.

The study is very well-designed and presented in a concise and logical manner. The use of evolution experiments to identify the mutations and then engineer them to quantify the epistatic effects and understand the mechanism behind them is very elegant. The real-world relevance is then supported by looking for these mutations in environmental samples. Despite this simplicity and clarity, in some places, the writing could be improved. I particularly found that the second half of the paper was not as easy to follow as the first part and could benefit from some clarifications. The figures could also contain a bit more information to help the reader.

Thank you!

1.1 For example, the abstract starts by talking about standing genetic variation but it's not immediately clear what is meant by that. Standing genetic variation seems to suggest that the resistance gene itself is present in the initial population, rather than variation in other loci that might affect the selection of the resistance gene. This could be better formulated.

We have revised the abstract to be clearer about the source of genetic variation.

1.2 The figures could be improved by being more specific about the datasets: are mutations in Figure 2 in the WT or the MCR-1 positive lines? Are the SNPs in Fig. 4A in lpxC? Do all isolates in Fig. 4 have the MCR-1 plasmid?

Thank you for the comment. We have edited the figure legend (line 128, page 5). Yes, Fig. 4A shows SNPs in lpxC, and all the isolates in Fig 4 have the MCR-1 plasmid. We have now clarified this in the figure legend (line 230, page 9).

1.3 Finally, the arguments being made about diversity in the different phylogroups were not very clear. This could be made more explicit at first mention, rather than later in the discussion section.

We have revised this section to clarify theses points (lines 242-245, page 10).

Reviewer #3 (Public Review):

Jangir et al. used an 'evolutionary ramp' experiment to evolve E. coli strains under the selection pressure of increasing colistin concentrations wherein the surviving fractions were collected for genomic analysis. They report that the mcr-1 carrying strain evolved higher colistin resistance much faster only in presence of lpxC mutations in the genome. They identify the mcr-1 and lpxC interactions to be positively epistatic and mutations only in lpxC do not lead to resistance to colistin. Taking a cue from their evolution experiments, they looked for the variations in lpxC sequences in the genomic datasets of clinical E. coli strains. They found many such variations in the genomes of clinical isolates. Importantly, they found those variations to be present even in non-resistant strains which might predispose those strains to gain untreatable levels of colistin resistance.

Strengths:

The study focuses on two key aspects of antibiotic resistance in clinical settings. First, is the antibiotic colistin itself which is part of the last line of defense. Second, is the importance of genomic variations in clinical isolates that have not been linked to any antibiotic resistance mechanisms. The data were presented in a logical sequence and maintained brevity. The link of lpxC to mcr-1 resistance is convincing.

Thank you!

Weaknesses:

The basic premise of the paper is solid but the following should be addressed.

3.1 In Figure 1, the authors applied the 'evolutionary ramp' method to isolate evolved strains with higher MIC to colistin; but, the conditions for the evolution of WT and strain carrying mcr-1 are different.Maintaining mcr-1 requires antibiotic selection which WT cannot withstand. Hence, if I am not mistaken, WT was not grown in the presence of any antibiotic.

The referee’s assertion that the selective pressures experienced by the WT and MCR+ populations were different is incorrect. We increased relative antibiotic dose (i.e., as a fraction of the MIC of the parental strains) at the same rate for both the WT and MCR+ populations. This is clearly explained in the text (lines 98-100, page 3), and the absolute colistin doses are shown in Figure 1. Please also see response 2.4 above.

In our study, we used a naturally occurring MCR-1 carrying plasmid from the IncX4 family. This plasmid is actually very stable (in the short term at least) in the absence of colistin, in spite of the costs imposed by MCR-1. We speculate that this stability in part reflect the high conjugation rate of the plasmids and the presence of a toxin-antitoxin module.

3.2 Not only that, maintaining a ~32 Kb plasmid itself can have different selective landscapes. The authors may replicate the experiment with their low-copy clone of mcr-1 which would make it easier for the authors to have an empty vector in WT as a proper control. Since now they know the expected mutations to be in lpxC, they might sequence a PCR amplicon of that region for validation of their hypothesis.

This is an interesting idea for a future study. We agree with the referee that the presence of the MCR-1 plasmid may impose additional selective pressures that could potentially lead to bacteria-plasmid co-evolution. However, our data suggests that bacteria-plasmid interactions were not an important selective force over the course of our experiment: we detected no mutations in the plasmid and almost all of the chromosomal mutations that we detected could be easily associated with selective pressures imposed by colistin.

3.3 In Figure 2, what are the effects of these mutations in lpxC? The authors state that many mutations map on to the metal binding domain; but are those significant changes? LpxC is relatively well characterized and authors may want to comment on these mutations a little more.

Yes, most of the evolved lines had mutations in the metal-binding domain site, and it is known that this site is very important for lpxC activity. For example, mutations at positions 79, 238, 242 and 246 lead to a hundred to thousand-fold decrease in lpxC activity (PMID: 24117400, 24108127, and 11148046), and many of our mutations map close to these sites (lines 140-143, page 6, and Figure 2b).

3.4 Also, lpxC mutations showed enrichment but lpxA did not. Is this suggestive of the type of Lipid A that is more preferred for the epistatic interactions? The authors may want to comment on that.

Interestingly, this could be the case that the epistatic interactions depend on the type of lipid A modification and the associated pleiotropic effects. Because mutations in LPS biosynthesis genes can have diverse adverse effects as it alters the membrane properties. However, in-depth future work is required to understand how the different types of changes in lipid A influence interactions with MCR. We chose not to further explore this in the paper, because lpxA was rarely mutated (2/17 clones) compared to lpxC (11/17 clones).

3.5 In Figure 3, the lpxC mutant shows a reduction in fitness in a competition assay. What is the growth pattern of individual strains?

The standard growth curve assay shows no significant difference in growth rate between LpxC mutant and wild-type strain (figure below). This is evident by the fact that standard growth curves are not ideal for capturing small differences in growth/fitness. Therefore, we emphasize the results of the competition experiment as this is gold standard method for measuring fitness effects (Figure 3c).

3.6 There is a possibility that slow growth of lpxC mutant provides benefit under antibiotic stress.

This is an interesting idea, but in this case, the slow growth of the lpxC mutant is clearly associated with a small decrease in colistin resistance (Figure 3A).

3.7 Minor comment: the three individual replicates shown in Figure 3a are all identical within a sample and do not add to the figure where n=3. The authors can simply show SD or report correct values of replicates.

We chose to show the raw data points, as this is the style of presentation that is being increasingly used by journals (i.e., many journals now say show all raw data points when n<6 or 10). It would not make sense to show a standard error as this was equal to 0.

3.8 In Figure 4, as the authors themselves have stated, the difference in heterogeneity could be simply due to variation within phylogroups and subsequent compositional differences within the populations. The authors must check if mutations were found in the same location of lpxA as found in their own evolved strains. Without this information, the heterogeneity data would be speculative. Adding the lpxC variants reported in figure 2 to the trees of figure 4 (right) will make it clear if their conclusion is justified.

This is an interesting point. We found no overlap between our experimentally evolved mutations and naturally occurring lpxC mutations, either at the level of nucleotides or codons. However, it is unclear if we should expect to see an overlap for two reasons: 1. The mutations present in natural isolates likely reflect a combination of beneficial mutations, neutral mutations, and weakly deleterious mutations. The mutations found in our evolved isolates, on the other hand, are all mutations that were beneficial under colistin selection. As such, it is probably not reasonable to expect a strong overlap between the two sets of mutations. 2. The lpxC mutations that we observed in our 11 lpxC mutated isolates are highly diverse – we found no cases of parallel evolution at the nucleotide level, and only a single example of parallel evolution at the codon level. Given this, our data suggest that a very wide diversity of sites of lpxC can interact epistatically with MCR-1 to increase colistin resistance. Again, this high diversity of potential lpxC mutations should give a weak association between lab evolved and clinical isolates.

We have added these points in the text (lines 278-304, pages 11-12).

3.9 The authors can perform a confirmatory experiment for the pre-existing part of their hypothesis. If they perform the evolutionary ramp experiment with a strain carrying lpxC mutant strain, will they see faster evolution of high MIC mutants?

This is an interesting idea, our results suggest that more rapid evolution of high level colistin resistance would occur in the lpxC mutant compared to a wild-type strain (assuming that both had an equivalent opportunity to acquire MCR-1 by horizontal gene transfer).

4.0 The rationale of how the presence of lpxC mutations can cause a strain without any colistin resistance to acquire mcr-1 is not addressed. The authors may want to comment on that.

MCR-1 is carried on conjugative plasmids, and the main plasmid families that carry MCR-1 (IncI2 and IncX4) have high conjugative rates. We have changed the text of introduction to emphasize that MCR-1 is carried on conjugative plasmids, and we have linked MCR-1 acquisition to plasmid conjugation (lines 327-328, page 13).

Autho Response

Reviewer #1 (Public Review):

Here the authors aimed to gain insight into the role of Septin-7 in skeletal muscle biology using a novel and powerful mouse model of inducible muscle specific septin-7 deletion. They combine this with CRISPR/Cas9 and shRNA mediated manipulation of Septin-7 in C2C12 cells in vitro to explore its role in muscle progenitor morphology and proliferation. There are a variety of interesting observations, with clear phenotypes induced by the Septin-7 manipulation, including effects on body weight, muscle force production, mitochondrial morphology, and cell proliferation. However each area is somewhat superficially examined, and certain conclusions require additional validation for robust support. Additionally, mechanistic insight into Septin 7's role is limited. Therefore, while the phenotypes are likely of intrigue to both the muscle and septin community, to significantly advance the field will require additional experimentation.

Specifically, it is currently difficult to distinguish between developmental and adult roles of Septin-7. The authors induce tamoxifen-mediated deletion at 1 month of age and examine muscle structure/function only at 4 months. By not studying early time points, it is difficult to determine whether particular phenotypes are directly due to Septin deletion or a secondary consequence of muscle atrophy and/or a decline in body weight. Further, by not inducing deletion at a later time point (i.e. after 2 months when muscle is generally matured), it is difficult to assess whether septin-7 plays a role in maintaining structure and function of mature muscle, or if its primary role is in muscle development.

We have conducted a number of trials for knocking-down of Septin-7 expression. These included Tamoxifen treatment of Cre- pregnant mothers, shorter treatments starting at early after birth, and treatments of adult animals. While the former led to still-born offsprings, the later resulted in only a minor – less than 20% - reduction of Septin-7 expression. These long trials led us to, on the one hand, concentrate on the protocol used throughout the manuscript (where a significant, up to 50%, reduction in the expression of the protein could be achieved) and to, on the other hand, focus also on myogenic cells in culture. This selection was also substantiated by the finding that Septin-7 expression is the highest in neonatal muscles and declines with age until adulthood (but remains essentially constant until an age of 18 months for the mice examined). As an identical Tamoxifen treatment of littermate Cre- mice did not result in any of the presented alterations (as demonstrated in the Supplementary material) we can conclude that they are the consequence of Septin-7 down-regulation. We, nonetheless, completely agree with the Reviewer that some observations are most likely indirect, i.e., are due to the loss of muscle mass. These include, e.g., the altered shape of the vertebra and the consequent “hunchback” phenotype. However, this observation further supports our claim that Septin-7 is essential for proper development of a normal musculature in these animals.

Further, the conclusion that septin-7 has an essential role in regeneration (seemingly based on expression increasing after injury) is unsupported and requires further experimentation where injury and regeneration is triggered in the absence of Septin-7 to establish a causative role.

We agree with the Reviewer that a clear causative role of Septin-7 in muscle regeneration would require a substantial amount of further experimentation on Septin-7 knock-down animals. We, however, believe that this – detailed description of the changes in transcription factors and key regulatory proteins together with changes in morphology in Septin-7 KD animals following muscle injury – is beyond the scope of the present manuscript and should be presented as a separate study. In this manuscript, however, we provide the essential background to substantiate this claim. We describe that fusion of myogenic cells is severely hindered if Septin-7 expression is suppressed while Septin-7 is upregulated following muscle injury to the extent which is significantly more than what would be expected if it would be simply due to the production of new muscle fibers.

Finally, there are intriguing observations in mitochondrial and myofiber organization and mitochondrial content; however further interrogation into additional relevant metrics of each, and at different time points of Septin-7 deletion, are needed to better understand these phenotypes and gain insight into Septin-7's role in their regulation.

Accepting the concern of the Reviewer we have conducted additional experiments to enable the proper characterization of the morphology. Additional relevant metrics – Aspect Ratios and Form Factors – have been calculated and are now incorporated into the revised MS and are presented in Figure 5.

Reviewer #2 (Public Review):

This is a comprehensive work describing for the first time the location and importance of the cytoskeletal protein Septin-7 in skeletal muscle. The authors, using a Septin-7 conditional knockdown mouse model, the C2C12 cell line, and enzymatically isolated adult muscle fibers, explore the normal location of this protein in muscle fibers, the morphological alterations in conditioned knockdown conditions, the developmental alterations, and the functional alterations in terms of force production. The global picture that emerges shows Septin-7 as a fundamental brick in both muscle construction, development, and regeneration; all this leads to reinforcing the basically structural nature of this protein role.

We thank the Reviewer for the appreciative words. We indeed believe that Septin-7 plays and important role in the proper organization and development of skeletal muscle. Even a partial knock-down of the protein at the early stages of life results in a severe loss in muscle mass accompanied by skeletal deformities. A complete knock-out of the protein results, at the myoblast level, in the inability of the cells to proliferate and form multinucleated cells confirming the essential role of this structural protein.

Reviewer #3 (Public Review):

This is an original study to explore the role of Septin-7, a cytoskeleton protein, in skeletal muscle physiology. The authors produced a unique mouse model with Septin-7 conditional knockdown specifically in skeletal muscle, which allowed them to examine the structure and function changes of skeletal muscle in response to the reduced protein expression level of Septin-7 in vivo and ex vivo at different development stages without the influence of other body parts with reduced Septin-7 expression. The study on the cellular model, C2C12 myoblast/myotubes with knockdown of Septin-7 expression, provided additional evidence of the importance of this cytoskeleton protein in regulating myoblast proliferation and differentiation. Majority of the data are supportive of the the major claim in this manuscript. However, additional key experiments and data analysis are needed to provide more mechanistic characterization of Septin-7 in muscle physiology.

We would like to express our thanks to the Reviewer for the critical comments on our manuscript and for the valuable suggestions that help substantiate our claim, that Septin-7 is an essential part of the cytoskeletal network in skeletal muscle and plays an important role in muscle differentiation as well as in myoblast proliferation and fusion.

A number of additional experiments were carried out to answer the comments/concerns of the Reviewer. Immunostaining of critical proteins (actin, myosin, and the L-type calcium channel) are now presented in Figure S4 for Cre+ animals. The T-tubules of enzymatically isolated fibers from these Septin-7 knock-down mice were also stained using Di-8-ANEPPS and the corresponding images are presented below. We describe how different Tamoxifen treatments at different time-points in the intra- and extra-uterine life of the animals resulted in the deletion of the SEPTIN 7 gene which ultimately led us to use the protocol (largest reduction with still viable mice) described in this manuscript. A more detailed description on how the fusion index, a clear marker a myotube differentiation, was conducted using desmin staining is now included and additional experiments (immunostaining and western blot) with MYH as suggested by the Reviewer are also presented. We carried out a thorough analysis of mitochondrial morphology (in line with the requirements of another Reviewer) and modified the corresponding figure in the revised MS accordingly.

Major Concerns:

1) The Septin-7 knockdown mouse model, the EM and IHC techniques are all established in the research group. It is a surprise to see that authors missed the opportunity to characterize the morphological changes in the T-tubule network, triad structure, the distribution of Ca release units (i.e., IHC of DHPR and RyR), and its co-localization with other key cytoskeletal proteins (i.e. actin) etc., in the muscle section or isolated muscle fibers.

We appreciate the reviewer's valuable critical comments. Even if we were not able to fully comply with all the requests, we corrected as many of the mentioned shortcomings as possible, by correcting the errors and to prove our claims with further experiments. Please find our responses to each critical remark below.

We conducted IHC staining on individual FDB fibers of C57Bl/6 mice presenting the distribution of skeletal muscle specific α-actinin, and RyR1 alongside with Septin-7 proteins (Figure 1E and F). As demonstrated in Figure 5E and F of the original MS (Figure 5 F and G in the revised version) normal triad structures were present both in Cre- and Cre+ muscle samples using EM analysis. However, the sarcomeres were distorted at places where large mitochondria appeared in Cre+ samples.

As suggested, T-tubule staining by Di-8-ANEPPS was carried out on isolated FDB fibers from Cre- and Cre+ animals, which revealed no considerable differences between the two groups.

Images present the T-tubule system of a single muscle fibers isolated from Cre- and Cre+ FDB muscle. Di-8-ANEPPS staining reveals no considerable difference between the two type of animals suggesting that the reduced Septin-7 expression does not alter the T-tubular system of skeletal muscle cells.

To further investigate the key components of muscle contraction and EC coupling, we carried out immunostaining in isolated single fibers from FDB muscle originating from Cre+ and Cre- mice. Immunocytochemistry revealed no significant alteration of actin, myosin 4, and L-type calcium channel labeling comparing the two mouse strains (see Figure S4 in the revised version).

2) The authors only studied one time point following the Tamoxifen treatment (4-month old with 3-month treatment). Based on Fig 2D, a significant body weight reduction was achieved after one month of the Tamoxifen treatment (at the age of 7 weeks), indicating a potential reduced muscle development at this age. Mice are considered fully matured at the age of 2 months. It will be more informative if the muscle samples and the in vivo and in vitro muscle activity are analyzed at this time point (7 or 8-week old), which should provide a direct answer if the knockdown of Septin-7 affects the muscle development. Additionally, a time dependent correlation of the level of Septin-7 knockdown with muscle function/morphology analysis should better define the role of Septin-7 in muscle development and function.

We agree with the Reviewer that Septin-7 has presumably more pronounced effect in the early stage of muscle development, since we detected higher expression level of the protein in muscle samples isolated from newborn and young as compared with adult animals. We conducted preliminarily in vivo and in vitro force experiments on 2-month-old mice after 1 month of Tamoxifen treatment. The grip force already decreased significantly in Cre+ mice but the decrease in twitch and tetanic force of EDL and Sol did not reach significance. These experiments were followed by the analysis of Septin-7 level in the muscle samples which showed less than 20% of reduction on average in the samples of Cre+ mice. This suggested that a more robust suppression of Septin-7 is needed to reach significant reduction in in vitro force thus we decided to extend the Tamoxifen treatment to 3 months.

3) Although the expression level of Septin-7 reduced during muscle development (Fig 1C), but its expression is still evident at the age of 4 months (Fig 1C and Fig S1F), indicating a potential role of Septin-7 in maintaining normal muscle function. It is important to examine whether the Tomaxifen treatment started after the muscle maturation at the age of 2-month old would affect the muscle structure and function. Particularly, these type of KD mice will be critical to answer if the KD will affect the regeneration rate following the muscle injury. The outcome will further test or support their claim of the essential roles of Septin-7 in muscle regeneration.

We agree with the Reviewer opinion that Septin-7 presumably plays an essential role not only during the early development of skeletal muscle but also in the matured tissue. In our preliminary studies Septin-7 protein expression was determined in skeletal muscle samples from mice at different developmental stage. As presented in Figure 1C we observed decrease in Septin-7 protein expression from newborn to adult stages. The expression profile of Septin-7 was also investigated in samples from 2, 4, 6, 9, and 18-month-old mice and a significant decrease was observed in samples isolated from mice of 4, 6, 9, and 18 months of age (58±8; 48±9; 66±16; 54±9% relative to the 2-month-old muscles, respectively), however there were no considerable changes between samples after 4 months of age.

In order to generate skeletal muscle specific, conditional Septin-7 knock-down animals, we applied Tamoxifen treatment at different developmental stages in our preliminary studies (see the table and figures below). When Cre- pregnant females were fed with Tamoxifen in the third trimester of pregnancy, it caused intrauterin lethality independent of the genotype. According to the animal ethics requirements we did not continue this experimental protocol. In the next stage of our initial experiments, 3 month-old mice were treated with both intraperitoneal injections for 5 consecutive days or Tamoxifen diet for 4 weeks. Here, only a moderate deletion of the exon4 was detected in SEPTIN 7 gene in Cre+ animals (data obtained from these mice are shown below).

These findings and the observation of ontogenesis dependent expression of Septin-7 indicated its significance at the early stage of development and suggested that we should try to modify the gene expression at earlier age. Six weeks of diet supplemented with Tamoxifen generated well detectable exon deletion in younger (1-month-old) mice. Regarding these observations we decided to start the Tamoxifen-supplemented diet in younger (4-week-old) animals immediately after separation from the mother and we continued the treatment for a longer period (3 months) to be sure that exon deletion will be prominent in all Cre+ animals.

Genetic modification of SEPTIN 7 gene following Tamoxifen treatment in mice mentioned above. RT-PCR

Figure presents the presence of floxed sites at SEPTIN 7 gene (white arrow) and the deletion of exon4 (red arrows) in the appropriate DNA samples isolated from mice treated with Tamoxifen from different age and using different methods and period of Tamoxifen application. Exon4 deletions were less than 20%, therefore these trials were not continued. Numbers above each lane correspond to the animal ID-s presented in the table above. Q – m. quadriceps, B- m. biceps femoris, P – m. pectoralis.

The knock-down of Septin-7 in the adult animals (where its expression is already low; see above) did not result in an appreciable further reduction. This led us to conclude that the role of Septin-7 is most pronounced in muscle development. In this framework, at the adult stage a possible function of Septin-7 in muscle regeneration following injury could be envisioned. This is demonstrated in Fiure 6 where we present that Septin-7 is upregulated following a mild injury. However, we believe, that a detailed examination of the role of Septin-7 in the regeneration is beyond the scope of the current manuscript and should be the basis of further studies.

4) Regarding the impact of Septin-7 on differentiation, it could be problematic if the images with the resolution shown in Figure S4A-C were used for fusion index calculation. If those are just zoomed in representative images and the authors used other lower resolution, global view images for quantification, those images are needed to be shown. The authors may also need to elaborate on why they stained Desmin instead of MYH for quantification of the fusion index of myotubes (page 27). Desmin also marks mesenchymal cells.

We apologize that the method used for fusion index calculation was not clear enough. Images in Figure S4A-C present the Septin-7 and actin cytoskeletal structure in proliferating myoblasts, before the induction of differentiation. Fusion index was determined in cultures where myotube differentiation was induced by reduced serum content (as described in Methods). We used desmin staining as the expression of this protein is present only in myotubes with 2 or more nuclei, where fusion of myoblasts has already started (see representative images below). Representative desmin-labeling images from control, scrambled and KD cultures are now included in Figure S5G at 5 days differentiated stage.

Figure presents two examples (bottom row is now added to Figure S5 as panel G) of the desmin-specific immunostaining used for the calculation of fusion index in the different C2C12 cultures. Specific signals of desmin are present following the fusion of single nuclei myoblast into myotubes (green), while non-differentiated myoblasts did not show immunolabeling for desmin. Nuclei are stained with DAPI (blue).

If Septin-7 is truly affecting differentiation, a decrease of MYH 2 expression can be readily detected by IHC or WB.

We are grateful for the Reviewer´s suggestion. We have conducted immunocytochemistry and WB experiments in proliferating myoblasts and myotubes at day 5 of differentiation. As the figure below demonstrates, myosin heavy chain-specific immunolabeling could be detected only in differentiated samples, while myoblasts did not show positive signal. However, there is a significantly lower number of MYH2-positive myotubes in Septin-7 KD cultures as compared with the control and scrambled samples. In addition, we detected decreased WB signal for MYH2 in Septin-7 KD protein samples compared with their control counterparts.

Figure presents the MYH2-specific immunostaining in the different C2C12 cultures. Specific signals of myosin heavy chain 2 (green) are present during myotube formation of differentiating cultures, however, less MYH2-positive myotubes are present in the Septin-7 KD cultures as a result of reduced capability of cells to fuse, here the DAPI-stained nuclei were only present. Proliferating myoblasts did not show specific immunolabeling for MYH2, as the confocal image and the appropriate part of the WB membranes show. We could also detect a decreased MYH2-specific labeling in Septin-7 KD samples as compared with the control ones using WB.

Additionally, Septin-7 may also affect the migration or fusion of myoblasts instead of differentiation. The observation of altered cell morphology and filopodia/lamellipodia formation (Figure 3C) in Septin7-KD cells before differentiation also implies a potential role of Septin-7 in migration. This possibility should be at least discussed.

We appreciate the Reviewer´s comment and suggestion. There are a few publication showing that alteration of septin (in some cases Septin-7) expression modifies the migration of different eukaryotic cell types, like in microvascular endothelial cells (PMID: 24451259), in human epithelial cells (PMID: 31905721), in neural crest cells (PMID: 2881782), and in human breast cancer or lung cancer cells (PMID: 27557506, 31558699, and 32516969). In the work of Li et al. (PMID:32382971) their findings revealed that miR-127-3p regulates myoblast proliferation by targeting Septin-7. In the present manuscript we described that Septin-7 modification alters myoblast fusion (Figure 3J), which is the accompanying phenomenon of differentiation. On the other hand, the effect of Septin-7 gene silencing on cell migration has been studied in detail and was presented to The Biophysical Society. The results are intended to be submitted as a separate manuscript.

5) The image shown in Figure 5F does not support the pooled data showed in Figure 5C. The size of mitochondria is remarkably lager in Cre+ muscle (Fig 5E and 5F). The morphology of mitochondria in Cre+ muscle are apparently normal (Fig 5F), while the mitochondrial DNA content are drastically reduced (Figure 5H), which is an important discovery and deserved to be further confirmed by WB and/or qPCR for critical mitochondrial proteins (i.e. MTCOX, COXV, etc.).

We thank the Reviewer for pointing out that the interpretation of images in Figure 5 was not clear enough. Based on this, and the on the clear request from the other Reviewer, a detailed evaluation of mitochondrial morphology was carried out and the panels of Figure 5 were redrawn and reorganized. The revised Figure 5 now presents the average Perimeter, the average Aspect Ratio, and the average Form Factor (panels C & H, for cross- & horizontal-sections, respectively), the relative distributions of the areas (panels D & I, for cross- & horizontal-sections, respectively), and the number of mitochondria normalized to fiber area (panel E, cross-sections). The mitochondrial DNA content is presented in panel J. As evidenced from these figures (and from the representative EM micro graphs), larger mitochondria, sometimes in large associations, are present in the muscles of Cre+ animals.

Furthermore, gene expression of four essential mitochondrial proteins cytochrome oxidase 1 (COX1), cytochrome oxidase 2 (COX2), succinate dehydrogenase (SDH), and ATP synthase) were determined in RNA samples from different skeletal muscles of Cre- and Cre+ animals using qPCR. As the figure below demonstrates there was a tendency of decreased expression of the aforementioned genes in Cre+ muscle samples, however, significant difference between the Cre- and Cre+ data could not be detected.

Figure represents the normalized mRNA expression of ATP synthase, SDH, COX1, and COX2 in Cre- (green) and Cre+ (red) samples isolated from m. quadriceps and m. pectoralis. Each gene expression was determined from 3 individual animals and a technical duplicate was used during the qPCR analysis. 36B4 gene encoding an acidic ribosomal phosphoprotein P0 was used as a normalizing gene.

6) Figure 2 H & I: It is unclear whether the muscle force was normalized to the individual muscle weight.

We are sorry about the incomplete representation and explanation of muscle force values. Figure 2F-I presents absolute force values without normalization to the cross sectional area. In order to answer the Reviewer´s comment the averages of normalized values are given in Table S3 in the modified manuscript.

7) The IHC results in Figure 6B are confusing. There are no centrally located nuclei in the Pax7 alone image of Figure 6B but abundant in the Pax7 + H&E image. The brown color of DAB and the purple color of hematoxylin are hard to be distinguished.

Images presenting the labeling of Pax7 (a transcription factor expressed in activated satellite cells) alone could not show centrally located nuclei, as the nuclei could only be visible when HE staining is applied. As the Reviewer mentioned brown color of DAB and the purple color of hematoxylin are sometimes difficult to distinguish, therefore, we first presented PAX7 expression visualized by DAB staining (localization was near the sarcolemma). In the next step we performed a double staining for PAX7 and HE to show both the cytoplasm and nuclei.

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:

We have now revised the manuscript to address the helpful comments and criticisms from the reviewers. The revised manuscript includes additional experiments demonstrating that inclusion of Csn2/Cas9 in the in vitro assays does not suppress the disintegration activity of Cas1-Cas2 to favor integration. These additional factors do not confer strand selectivity on integration either. Furthermore, the results of integration reactions using substrates mimicking PAM-containing pre- spacers have also been added.

New figures and figure modifications at a glance:

1) The new Figure 2 shows Cas1-Cas2 reactions in a linear target site and the effects of Csn2 and/or Cas9 on proto-spacer insertion into this target (Reviewer 1).

The original Figure 2 (with slight modifications) is now moved to ’Supplementary Data’ as Figure 2-figure supplement 2, and shows proto-spacer insertion by Cas1-Cas2 into a nicked linear target site (Reviewer 2). Figure 2 is the only one in the main set of figures that has been extensively modified.

2) The new Figure 2-figure supplement 1 (under ‘Supplementary Data’) shows the effects of Csn2, Cas9 or both on proto-spacer integration-disintegration by Cas1-Cas2 when the target site is present in a supercoiled plasmid (Reviewer 1).

3) The new Figure 4-figure supplement 1 lists the sequences of the full- and half-target sites used for the reactions shown in Figure 4 (Reviewer 2).

4) The new Figure 2-figure supplement 3 shows the insertion properties of PAM-containing pre- spacer mimics in reactions with Cas1-Cas2 alone or supplemented with Csn2, Cas9 or both (Reviewer 1).

5) The new Figure 6-figure supplement 1 gives a structural perspective of the trombone substrates used for the reactions shown in Figure 6B, C (Reviewer 1).

6) The original Supplementary Figure S8 showing assays for PAM-specific cleavage by Cas1- Cas2 has been removed (Reviewer 1).

7) There are no changes in the other figures under ‘Supplementary Data’, although several have new numbers consistent with the revisions made.

Public Review (Reviewers #1 and #2):

The present work is a critical extension of the in vitro biochemical activities of the Cas1- Cas2 complex described by Wright and Doudna (Nat Struct Mol Biol, 2016; 23: 876-883). We have kept all experimental conditions nearly identical to those used by these authors to make the results from the two studies directly comparable. Importantly, we now show that the prior model for proto-spacer integration into the CRISPR locus by Cas1-Cas2 is an oversimplification of a much more nuanced mechanism.

While both reviewers recognize the importance of our findings in challenging the current thinking on the adaptation mechanism of CRISPR immunity, they express reservations as to whether the in vitro results recapitulate the in vivo mechanism of spacer acquisition. This seems to us to be too broad a criticism from which few (if any) biochemical experiments can be immune.

Our key finding is that disintegration during the second step of proto-spacer integration generates a DNA structure that has all the hallmarks of a DNA damage intermediate that the bacterial repair machinery can readily process into an authentic integration product. We invoke no new or ad hoc mechanisms, and the model we propose fits neatly into the DNA gap-filling mechanisms known to operate in DNA transposition pathways.

The proto-spacer is functionally a ‘micro-transposon’, whose shortness imposes severe torsional strain on the transposition intermediate that precedes the final integration product. In vitro experiments suggest that transcription is potentially capable of resolving this intermediate (Budhathoki et al., Nat Struct Mol Biol, 2020, 27: 489-99). In principle, replication can also accomplish this task. Our study now demonstrates that simply nicking the DNA (disintegration) is an equally effective solution for relieving the topological stress accompanying integration. DNA loose ends can then be readily tied up by the bacterial repair machinery.

We concur with the concluding sentence of reviewer 2, “The simple conclusion that Cas1- Cas2 catalyzed hydrolysis of a phosphodiester may relieve strain and allow productive transposition to occur doesn’t get emphasized enough in my opinion.” We have now expanded on this point in the revised ‘Discussion’.

Reviewer #1:

In addition, the in vitro system used here is only partially reconstituted. The substrates lack a PAM sequence, which is necessary for protospacers to be incorporated in the correct orientation and may help direct the first integration event to the L-R junction. Presumably because of this all the reactions presented do not analyze the orientation of the incorporated prespacer sequence. Cas9 and Csn2 are also absent (as are other potentially required host factors), which are necessary for correct integration in vivo.

1A. Strand specificity: The in vitro integration reactions with the Cas1-Cas2 complex were done using a protospacer of the optimal size (26 nt on each strand with the four 3’- proximal bases on each strand as unpaired). Either proto-spacer strand is equally competent to initiate the strand transfer reaction, as could be inferred from Figure 3 of the original submission. Here, reactions utilized modified proto-spacers that differed in their top and bottom strand lengths. They gave two insertion products (IP) each at the L-R (leader-repeat) and R-S (repeat-spacer) junctions of a normal target site. In modified targets in which integration was limited to just the L- R junction, two insertion products were formed. One panel of Figure 3 (which is retained in the revised manuscript) showing the four insertion products from the normal target (lane 10) and two from the modified targets (lanes 11-13) for a protospacer with 26 nt and 31 nt long strands is displayed below.

The ability of either proto-spacer strand to initiate integration is now more directly shown in Figure 2 (new) of the revised manuscript. Here the labeled top or bottom strand of the proto- spacer (PS) gave insertion products (IP) at the L-R and R-S junctions of the target site. Panel B of Figure 2 (pasted below) demonstrates this result.

1B. Cas9, Csn2 included reactions: The data for reactions containing Csn2 or Cas9 or both were not shown previously, as they did not alter Cas1-Cas2 activity by promoting strand specificity of integration or suppressing disintegration. These results are now shown in the revised Figure 2 (linear target) and the new Figure 2-figure supplement 1 (supercoiled target). Portions of these figures are shown below.

The relevant revised text describing the lack of strand specificity to proto-spacer integration by Cas1-Cas2 and the Csn2/Cas9 effects on integration is pasted below.

Page 15, lines 229-235.

"Unlike orientation-specific proto-spacer integration in vivo, Cas1- Cas2 reactions in vitro showed no strand-specificity (Figure 2B). This bias-free insertion of the top or bottom strand from the proto-spacer was unchanged by the addition of Csn2 or Cas9 or both to the reactions (Figure 2C-E). These proteins, singly or in combiantion, also failed to stabilize proto-spacer integrations in the supercoiled plasmid target (Figure 2-figure supplement 1). Instead, they inhibited plasmid relaxation. Inhibition could occur at the level of integration per se or strand rotation during integration-disintegration"

1C. PAM-containing substrates: We have now tested Cas1-Cas2 activity (with and without added Csn2 or Cas9 or both) on PAM-containing substrates that mimic ‘pre-spacers’, Figure 2- figure supplement 3 (new).

In these substrates, a proto-spacer strand of the standard length (26 nt; lacking PAM or its complement) is inserted at the L-R junction with higher efficiency than the longer strand (containing PAM or its complement). Following the first integration at L-R, the pre-spacer mimics containing > 26 nt in one strand or both strands are inhibited in the second strand transfer to the R-S junction. A portion of Figure 2-figure supplement 3 illustrating theses points is shown below.

The revised ‘Results’ section has the following added description of the activities of PAM- containing pre-spacer mimics.

Pages 16-19, lines 265-297. Cas1-Cas2 activity on pre-spacer mimics carrying the PAM sequence

"The strand cleavage and strand transfer steps of proto-spacer insertion at the CRISPR locus must engender safeguards against self-targeting of the inserted spacer as well as its non-functional orientation. However, no strand selectivity is seen in the in vitro Cas1-Cas2 reactions with already processed proto-spacers lacking the PAM sequence (Figures 2 and 3). By coordinating PAM- specific cleavage of a pre-spacer with transfer of this cleaved strand to the L-R junction, the inserted spacer will be in the correct orientation to generate a functional crRNA. To examine this possibility, we tested the integration characteristics of pre-spacer mimics containing the PAM sequence.

The inclusion of PAM or PAM and its complement in the integration substrates (Figure 2- figure supplement 3A) did not confer strand specificity on reactions with Cas1-Cas2 alone or with added Csn2, Cas9 or both (Figure 2-figure supplement 3B-E). Optimal integration by Cas1-Cas2 occurred with the 26 nt strands of the native protospacer with their 4 nt 3’-overhangs (Figure 2- figure supplement 3B-E; lanes 2). The pre-spacer mimics containing one or both > 26 nt strands had reduced integration competence (Figure 2-figure supplement 3B-E; lanes 4). Even here, the 26 nt strand with the 4 nt overhang (Figure 2-figure supplement 3C; lane 4) was preferred in integration over the longer 29nt PAM-containing strand (Figure 2-figure supplement 3D; lane 4) or the 33 nt PAM complement-containing strand (Figure 2-figure supplement 3E; lane 4). In contrast to the processed proto-spacer that gave nearly equal integration at L-R and R-S, IP(L- R) ≈ IP(R-S) (Figure 2-figure supplement 3B-E; lanes 2), the longer pre-spacer mimics were inhibited in integration at R-S, IP(L-R) > IP(R-S) (Figure 2-figure supplement 3B-E lanes 4). This is the expected outcome if the initial strand transfer occurs at L-R, and a ruler-like mechanism orients the reactive 3’-hydroxyl for the second strand transfer at R-S. This sequential two-step scheme for proto-spacer integration is consistent with the results shown in Figure 3 as well. These reaction features were not modulated by Csn2 or Cas9 (Figure 2-figure supplement 3B-E; lanes 6 and 8), although Csn2 plus Cas9 was inhibitory (Figure 2-figure supplement 3B-E; lanes 10).

There is no evidence for integration accompanying PAM-specific cleavage in our in vitro reactions. In the E. coli CRISPR system, Cas1-Cas2 is apparently sufficient for PAM-specific cleavage in vitro (22). By contrast, in the S. pyogenes system, cleavage is attributed to Cas9 or as yet uncharacterized bacterial nuclease(s) (35). The mechanism for generating an integration- proficient and orientation-specific proto-spacer, which may not be conserved among CRISPR systems, is poorly understood at this time."

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 #1 (Public Review):

The role of the parietal (PPC), the retrospenial (RSP) and the the visual cortex (S1) was assessed in three tasks corresponding a simple visual discrimination task, a working-memory task and a two-armed bandit task all based on the same sensory-motor requirements within a virtual reality framework. A differential involvement of these areas was reported in these tasks based on the effect of optogenetic manipulations. Photoinhibition of PPC and RSP was more detrimental than photoinhibition of S1 and more drastic effects were observed in presumably more complex tasks (i.e. working-memory and bandit task). If mice were trained with these more complex tasks prior to training in the simple discrimination task, then the same manipulations produced large deficits suggesting that switching from one task to the other was more challenging, resulting in the involvement of possibly larger neural circuits, especially at the cortical level. Calcium imaging also supported this view with differential signaling in these cortical areas depending on the task considered and the order to which they were presented to the animals. Overall the study is interesting and the fact that all tasks were assessed relying on the same sensory-motor requirements is a plus, but the theoretical foundations of the study seems a bit loose, opening the way to alternate ways of interpreting the data than "training history".

1) Theoretical framework:

The three tasks used by the authors should be better described at the theoretical level. While the simple task can indeed be considered a visual discrimination task, the other two tasks operationally correspond to a working-memory task (i.e. delay condition which is indeed typically assessed in a Y- or a T-maze in rodent) or a two-armed bandit task (i.e. the switching task), respectively. So these three tasks are qualitatively different, are therefore reliant on at least partially dissociable neural circuits and this should be clearly analyzed to explain the rationale of the focus on the three cortical regions of interest.

We are glad to see that the reviewer finds our study interesting overall and sees value in the experimental design. We agree that in the previous version, we did not provide enough motivation for the specific tasks we employed and the cortical areas studied.

Navigating to reward locations based on sensory cues is a behavior that is crucial for survival and amenable to a head-fixed laboratory setting in virtual reality for mice. In this context of goal-directed navigation based on sensory cues, we chose to center our study on posterior cortical association areas, PPC and RSC, for several reasons. RSC has been shown to be crucial for navigation across species, poised to enable the transformation between egocentric and allocentric reference frames and to support spatial memory across various timescales (Alexander & Nitz, 2015; Fischer et al., 2020; Pothuizen et al., 2009; Powell et al., 2017). It furthermore has been shown to be involved in cognitive processes beyond spatial navigation, such as temporal learning and value coding (Hattori et al., 2019; Todd et al., 2015), and is emerging as a crucial region for the flexible integration of sensory and internal signals (Stacho & ManahanVaughan, 2022). It thus is a prime candidate area in the study of how cognitive experience may affect cortical involvement in goal-directed navigation.

RSC is heavily interconnected with PPC, which is generally thought to convert sensory cues into actions (Freedman & Ibos, 2018) and has been shown to be important for navigation-based decision tasks (Harvey et al., 2012; Pinto et al., 2019). Specific task components involving short-term memory have been suggested to cause PPC to be necessary for a given task (Lyamzin & Benucci, 2019), so we chose such task components in our complex tasks to maximize the likelihood of large PPC involvement to compare the simple task to.

One such task component is a delay period between cue and the ultimate choice report, which is a common design in decision tasks (Goard et al., 2016; Harvey et al., 2012; Katz et al., 2016; Pinto et al., 2019). We agree with the reviewer that traditionally such a task would be referred to as a workingmemory task. However, we refrain from using this terminology because it may cause readers to expect that to solve the task, mice use a working-memory dependent strategy in its strictest and most traditional sense, that is mice show no overt behaviors indicative of the ultimate choice until the end of the delay period. If the ultimate choice is apparent earlier, mice may use what is sometimes referred to as an embodiment-based strategy, which by some readers may be seen as precluding working memory. Indeed, in new choice-decoding analyses from the mice’s running patterns, we show that mice start running towards the side of the ultimate choice during the cue period already (Figure 1—figure supplement 1). Regardless of these seemingly early choices, however, we crucially have found much larger performance decrements from inhibition in mice performing the delay task compared to mice performing the simple task, along with lower overall task performance in the delay task, indicating that the insertion of a delay period increased subjective task difficulty. As traditional working-memory versus embodiment-based strategies are not the focus of our study here and do not seem to inform the performance decrements from inhibition, we chose to label the task descriptively with the crucial task parameter rather than with the supposedly underlying cognitive process.

For the switching task, we appreciate that the reviewer sees similarities to a two-armed bandit task. However, in a two-armed bandit task, rewards are typically delivered probabilistically, whereas in our task, cue and action values are constant within each of the two rule blocks, and only the rule, i.e. the cuechoice association, reverses across blocks. This is a crucial distinction because in our design, blocks of Rule A in the switching task are identical to the simple task, with fixed cue-choice associations and guaranteed reward delivery if the correct choice is made, allowing a fair comparison of cortical involvement across tasks.

We have now heavily revised the introduction, results, and discussion sections of the manuscript to better explain the motivation for the tasks and the investigated brain areas. These revisions cover all the points mentioned in this response.

Furthermore, we agree with the reviewer that the three tasks are qualitatively different and likely depend on at least partially dissociable circuits. We consider the large differences in cortical inhibition effects between the simple and the complex tasks as evidence for this notion. We also want to highlight that in fact, we performed task-specific optogenetic manipulations presented in the Supplementary Material to further understand the involvement of different areas in task-specific processes. In what is now Figure 1—figure supplement 4, we restricted inhibition in the delay task to either the cue period only or delay period only, finding that interestingly, PPC or RSC inhibition during either period caused larger performance drops than observed in the simple task. We also performed epoch-specific inhibition of PPC in the switching task, targeting specifically reward and inter-trial-interval periods following rule switches, in what is now Figure 1—figure supplement 5. With such PPC inhibition during the ITI, we observed no effect on performance recovery after rule switches and thus found PPC activity to be dispensable for rule updates.

For the working-memory task we do not know the duration of the delay but this really is critical information; per definition, performance in such a task is delay-dependent, this is not explored in the paper.

We thank the reviewer for pointing out the lack of information on delay duration and have now added this to the Methods section.

We agree that in classical working memory tasks where the delay duration is purely defined by the experimenter and varied throughout a session, performance is typically dependent on delay duration. However, in our delay task, the delay distance is kept constant, and thus the delay is not varied by the experimenter. Instead, the time spent in the delay period is determined by the mouse, and the only source of variability in the time spent in the delay period is minor differences in the mice’s running speeds across trials or sessions. Notably, the differences in time in the delay period were greatest between mice because some mice ran faster than others. Within a mouse, the time spent in the delay period was generally rather consistent due to relatively constant running speeds. Also, because the mouse had full control over the delay duration, it could very well speed up its running if it started to forget the cue and run more slowly if it was confident in its memory. Thus, because the delay duration was set by the mouse and not the experimenter, it is very challenging or impossible to interpret the meaning and impact of variations in the delay duration. Accordingly, we had no a priori reason to expect a relationship between task performance and delay duration once mice have become experts at the delay task. Indeed, we do not see such a relationship in our data (see plot here, n = 85 sessions across 7 mice). In order to test the effect of delay duration on behavioral performance, we would have to systematically change the length of the delay period in the maze, which we did not do and which would require an entirely new set of experiments.

Also, the authors heavily rely on "decision-making" but I am genuinely wondering if this is at all needed to account for the behavior exhibited by mice in these tasks (it would be more accurate for the bandit task) as with the perspective developed by the authors, any task implies a "decision-making" component, so that alone is not very informative on the nature of the cognitive operations that mice must compute to solve the tasks. I think a more accurate terminology in line with the specific task considered should be employed to clarify this.

We acknowledge that the previous emphasis on decision-making may have created expectations that we demonstrate effects that are specific to the ‘decision-making’ aspect of a decision task. As we do not isolate the decision-making process specifically, we have substantially revised our wording around the tasks and removed the emphasis on decision-making, including in the title. Rather than decision-making, we now highlight the navigational aspect of the tasks employed.

The "switching"/bandit task is particularly interesting. But because the authors only consider trials with highest accuracy, I think they are missing a critical component of this task which is the balance between exploiting current knowledge and the necessity to explore alternate options when the former strategy is no longer effective. So trials with poor performance are thus providing an essential feedback which is a major drive to support exploratory actions and a critical asset of the bandit task. There is an ample literature documenting how these tasks assess the exploration/exploitation trade-off.

We completely agree with the reviewer that the periods following rule switches are an essential part of the switching task and of high interest. Indeed, ongoing work in the lab is carefully quantifying the mice’s strategy in this task and exploring how mice use errors after switches to update their belief about the rule. In this project, however, a detailed quantification of switching task strategy seemed beyond the scope because our focus was on training history and not on the specifics of each task. While we agree with the reviewer about the interesting nature of the switching period, it would be too much for a single paper to investigate the detailed mechanisms of each task on top of what we already report for training history. Instead, we have now added quantifications of performance recovery after rule switches in Figure 1— figure supplement 2, showing that rule switches cause below-chance performance initially, followed by recovery within tens of trials.

2) Training history vs learning sets vs behavioral flexibility:

The authors consider "training history" as the unique angle to interpret the data. Because the experimental setup is the same throughout all experiments, I am wondering if animals are just simply provided with a cognitive challenge assessing behavioral flexibility given that they must identify the new rule while restraining from responding using previously established strategies. According to this view, it may be expected for cortical lesions to be more detrimental because multiple cognitive processes are now at play.

It is also possible that animals form learning sets during successive learning episodes which may interfere with or facilitate subsequent learning. Little information is provided regarding learning dynamics in each task (e.g. trials to criterion depending on the number of tasks already presented) to have a clear view on that.

We thank the reviewer for raising these interesting ideas. We have now evaluated these ideas in the context of our experimental design and results. One of the main points to consider is that for mice transitioned from either of the complex tasks to the simple task, the simple task is not a novel task, but rather a well-known simplification of the previous tasks. Mice that are experts on the delay task have experienced the simple task, i.e. trials without a delay period, during their training procedure before being exposed to delay periods. Switching task expert mice know the simple task as one rule of the switching task and have performed according to this rule in each session prior to the task transition. Accordingly, upon to the transition to the simple task, both delay task expert mice and switching task expert mice perform at very high levels on the very first simple task session. We now quantify and report this in Figure 2—figure supplement 1 (A, B). This is crucial to keep in mind when assessing ‘learning sets’ or ‘behavioral flexibility’ as possible explanations for the persistent cortical involvement after the task transitions. In classical learning sets paradigms, animals are exposed to a series of novel associations, and the learning of previous associations speeds up the learning of subsequent ones (Caglayan et al., 2021; Eichenbaum et al., 1986; Harlow, 1949). This is a distinct paradigm from ours because the simple task does not contain novel associations that are new to the mice already trained on the complex tasks. Relatedly, the simple task is unlikely to present a challenge of behavioral flexibility to these mice given our experimental design and the observation of high simple task performance in the first session after the task transition.

We now clarify these points in the introduction, results, and discussion sections, also acknowledging that it will be of interest for future work to investigate how learning sets may affect cortical task involvement.

3) Calcium imaging data versus interventions:

The value of the calcium imaging data is not entirely clear. Does this approach bring a new point to consider to interpret or conclude on behavioral data or is it to be considered convergent with the optogenetic interventions? Very specific portions of behavioral data are considered for these analyses (e.g. only highly successful trials for the switching/bandit task) and one may wonder if considering larger or different samples would bring similar insights. The whole take on noise correlation is difficult to apprehend because of the same possible interpretation issue, does this really reflect training history, or that a new rule now must be implemented or something else? I don't really get how this correlative approach can help to address this issue.

We thank the reviewer for pointing out that the relationship between the inhibition dataset and calcium imaging dataset is not clear enough. We restricted analyses of inhibition and calcium imaging data in the switching task to the identical cue-choice associations as present in the simple task (i.e. Rule A trials of the switching task). We did this because we sought to make the fairest and most convincing comparison across tasks for both datasets. However, we can now see that not reporting results with trials from the other rule causes concerns that the reported differences across tasks may only hold for a specific subset of trials.

We have now added analyses of optogenetic inhibition effects and calcium imaging results considering Rule B trials. In Figure 1—figure supplement 2, we show that when considering only Rule B trials in the switching task, effects of RSC or PPC inhibition on task performance are still increased relative to the ones observed in mice trained on and performing the simple task. We also show that overall task performance is lower in Rule B trials of the switching task than in the simple task, mirroring the differences across tasks when considering Rule A trials only.

We extended the equivalent comparisons to the calcium imaging dataset, only considering Rule B trials of the switching task in Figure 4—figure supplement 3. With Rule B trials only, we still find larger mean activity and trial-type selectivity levels in RSC and PPC, but not in V1, compared to the simple task, as well as lower noise correlations. We thus find that our conclusions about area necessity and activity differences across tasks hold for Rule B trials and are not due to only considering a subset of the switching task data.

In Figure 4—figure supplement 4, we further leverage the inclusion of Rule B trials and present new analyses of different single-neuron selectivity categories across rules in the switching task, reporting a prevalence of mixed selectivity in our dataset.

Furthermore, to clarify the link between the optogenetic inhibition and the calcium imaging datasets, we have revised the motivation for the imaging dataset, as well as the presentation of its results and discussion. Investigating an area’s neural activity patterns is a crucial first step towards understanding how differential necessity of an area across tasks or experience can be explained mechanistically on a circuit level. We now elaborate on the fact that mechanistically, changes in an area’s necessity may or may not be accompanied by changes in activity within that area, as previous work in related experimental paradigms has reported differences in necessity in the absence of differences in activity (Chowdhury & DeAngelis, 2008; Liu & Pack, 2017). This phenomenon can be explained by differences in the readout of an area’s activity. We now make more explicit that in contrast to the scenario where only the readout changes, we find an intriguing correspondence between increased necessity (as seen in the inhibition experiments) and increased activity and selectivity levels (as seen in the imaging experiments) in cortical association areas depending on the current task and previous experience. Rather than attributing the increase in necessity solely to these observed changes in activity, we highlight that in the simple task condition already, cortical areas contain a high amount of task information, ruling out the idea that insufficient local information would cause the small performance deficits from inhibition. Our results thus suggest that differential necessity across tasks and experience may still require changes at the readout level despite changes in local activity. We view our imaging results as an exciting first step towards a mechanistic understanding of how cognitive experience affects cortical necessity, but we stress that future work will need to test directly the relationship between cortical necessity and various specific features of the neural code.

Reviewer #2 (Public Review):

The authors use a combination of optogenetics and calcium imaging to assess the contribution of cortical areas (posterior parietal cortex, retrosplenial cortex, S1/V1) on a visual-place discrimination task. Headfixed mice were trained on a simple version of the task where they were required to turn left or right depending on the visual cue that was present (e.g. X = go left; Y = go right). In a more complex version of the task the configurations were either switched during training or the stimuli were only presented at the beginning of the trial (delay).

The authors found that inhibiting the posterior parietal cortex and retrosplenial cortex affected performance, particularly on the complex tasks. However, previous training on the complex tasks resulted in more pronounced impairments on the simple task than when behaviourally naïve animals were trained/tested on a simple task. This suggests that the more complex tasks recruit these cortical areas to a greater degree, potentially due to increased attention required during the tasks. When animals then perform the simple version of the task their previous experience of the complex tasks is transferred to the simple task resulting in a different pattern of impairments compared to that found in behaviorally naïve animals.

The calcium imaging data showed a similar pattern of findings to the optogenetic study. There was overall increased activity in the switching tasks compared to the simple tasks consistent with the greater task demands. There was also greater trial-type selectivity in the switching task compared to the simple task. This increased trial-type selectivity in the switching tasks was subsequently carried forward to the simple task so that activity patterns were different when animals performed the simple task after experiencing the complex task compared to when they were trained on the simple task alone

Strengths:

The use of optogenetics and calcium-imaging enables the authors to look at the requirement of these brain structures both in terms of necessity for the task when disrupted as well as their contribution when intact.

The use of the same experimental set up and stimuli can provide a nice comparison across tasks and trials.

The study nicely shows that the contribution of cortical regions varies with task demands and that longerterm changes in neuronal responses c can transfer across tasks.

The study highlights the importance of considering previous experience and exposure when understanding behavioural data and the contribution of different regions.

The authors include a number of important controls that help with the interpretation of the findings.

We thank the reviewer for pointing out these strengths in our work and for finding our main conclusions supported.

Weaknesses:

There are some experimental details that need to be clarified to help with understanding the paper in terms of behavior and the areas under investigation.

The use of the same stimuli throughout is beneficial as it allows direct comparisons with animals experiencing the same visual cues. However, it does limit the extent to which you can extrapolate the findings. It is perhaps unsurprising to find that learning about specific visual cues affects subsequent learning and use of those specific cues. What would be interesting to know is how much of what is being shown is cue specific learning or whether it reflects something more general, for example schema learning which could be generalised to other learning situations. If animals were then trained on a different discrimination with different stimuli would this previous training modify behavior and neural activity in that instance. This would perhaps be more reflective of the types of typical laboratory experiments where you may find an impairment on a more complex task and then go on to rule out more simple discrimination impairments. However, this would typically be done with slightly different stimuli so you don't introduce transfer effects.

We agree with the reviewer that investigating the effects of schema learning on cortical task involvement is an exciting future direction and have now explicitly mentioned this in the Discussion section. As the reviewer points out, however, our study was not designed to test this idea specifically. Because investigating schema learning would require developing and implementing an entirely new set of behavioral task variants, we feel this is beyond the scope of the current work. As to the question of how generalized the effects of cognitive experience are, our data in the run-to-target task suggest that if task settings are sufficiently distinct, cortical involvement can be similarly low regardless of complex task experience (now Figure 3—figure supplement 1). This finding is in line with recent work from (Pinto et al., 2019), where cortical involvement appears to change rapidly depending on major differences in task demands. However, work in MT has shown that previous motion discrimination training using dots can alter MT involvement in motion discrimination of gratings (Liu & Pack, 2017), highlighting that cortical involvement need not be tightly linked to the sensory cue identity.

It is not clear whether length of training has been taken into account for the calcium imaging study given the slow development of neural representations when animals acquire spatial tasks.

We apologize that the training duration and the temporal relationship between task acquisition and calcium imaging was not documented for the calcium imaging dataset. Please see our detailed reply below the ‘recommendations for the authors’ from Reviewer 2 below.

The authors are presenting the study in terms of decision-making, however, it is unclear from the data as presented whether the findings specifically relate to decision making. I'm not sure the authors are demonstrating differential effects at specific decision points.

We understand that the previous emphasis on decision-making may have created expectations that we demonstrate effects that are specific to the ‘decision-making’ aspect of a decision task. As we do not isolate the decision-making process specifically, we have substantially revised our wording around the tasks and removed the emphasis on decision-making, including in the title. Rather than decision-making, we now highlight the navigational aspect of the tasks employed.

While we removed the emphasis on the decision-making process in our tasks, we found the reviewer’s suggestion to measure ‘decision points’ a useful additional behavioral characterization across tasks. So, we quantified how soon a mouse’s ultimate choice can be decoded from its running pattern as it progresses through the maze towards the Y-intersection. We now show these results in Figure 1—figure supplement 1. Interestingly, we found that in the delay task, choice decoding accuracy was already very high during the cue period before the onset of the delay. Nevertheless, we had shown that overall task performance and performance with inhibition were lower in the delay task compared to the simple task. Also, in segment-specific inhibition experiments, we had found that inhibition during only the delay period or only the cue period decreased task performance substantially more than in the simple task, thus finding an interesting absence of differential inhibition effects around decision points. Overall, how early a mouse made its ultimate decision did not appear predictive of the inhibition-induced task decrements, which we also directly quantify in Figure 1—figure supplement 1.

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 #1 (Public Review):

In this paper, Bai et al. investigate in experiments and simulations how cohesion is maintained in chemotactic travelling waves of bacteria. These waves emerge from the bacterial population consuming an attractant, thus carving a gradient which they follow chemotactically. This paper builds up on previous work of some of the authors (Fu et al, Nat Commun 2018), which found that in these waves bacteria with varying degree of chemotactic sensitivity organize spatially in the band, which allows for its cohesiveness despite varying phenotypes. The authors investigate here an additional element for the cohesiveness of the wave: because the sharpness of the gradient increases from the front to the back of the wave, 'late' cells catch up via a stronger chemotactic response, and front cells slow down via a weaker one. This had been already postulated in earlier work on the phenomenon (Saragosti et al. PNAS 2011), but here the authors investigate how this applies to cells with varying chemotactic sensitivity. They also performed agent-based simulations of the cells behavior in the gradient and developed a model of the motion in the gradient. The latter maps the spatial dependence of the gradient steepness onto an effective travelling potential which keeps the cells together in a group as the gradient and the wave propagate. Importantly, the effective potential is predicted to be tighter for cells with higher chemotactic sensitivity, in agreement with the cell behavior they observe in experiments where the chemotactic sensitivity is artificially modulated. This suggests that weakly chemotactic cells are more weakly bound to the group and have a higher chance of being left behind. This last part is interesting in the context of range extension in semi-solid agar, where bacteria are known to be spatially organized and selected according to their chemotactic motility (Ni et al, Cell reports 2017, Liu et al Nature 2019)

This paper builds its strengths on the extensive experimental characterization of the system and a variety of modeling approaches and makes a fairly convincing case for the way of understanding the mechanism of cohesion maintenance they propose.

In fact, we have addressed both the mechanism to maintain a coherent group and also the mechanism to form ordered pattern of diverse phenotypes. Thanks to the reviewer, we noticed that the second point was not clearly showed out in our previous version. So that we have largely rewritten the texts and reorganized the results to prominent both mechanism.

From a methodological perspective, only a few points need to be addressed:

Control experiments need to quantify the cell-to-cell variability of the induction level of Tar by tetracycline.

The distributions of the titrate cells are presented by a ptet-Tar-GFP strain, where the GFP is used as a reporter of the expressed Tar protein. The results are shown below:

Chemical attraction to cues released by other cells is a well-documented way to create cohesive large scale structures in E. coli (Budrene & Berg Nature 1995, Park et al PNAS 2003, Jani et al Microbiology 2017, Laganenka et al Nat commun 2016). The cohesion of the wave have never been analyzed in this optic, despite being a possible alternative explanation to the gradient shape. Since the authors main claim is about the wave cohesion, they should provide evidence that such an explanation can be ruled out or considered secondary.

We thank the reviewer to point out the self-attractant secretion as a possible mechanism to maintain coherent group. We argue that this mechanism is not necessary for the chemotactic group to maintain coherency, because the migration group keeps without considering these effect in our agent based simulations.

Moreover, as suggested by the reviewer, we Used a Tar only strain, which do not sense any chemo-attractant other than aspartate, to show that the migration group maintained coherent (see Fig S9). This experiment showed that the secretion of self-attractant is not essential for the coherent group migration.

Possible effects of physical interactions between cells on the chemotactic response are not accounted for. The consequences should be better discussed, because they are known to influence chemotactic motility at the densities encountered in the present experiments (Colin et al Nat commun 2019).

As being reported by Colin et al., the effective drift velocity and the chemotactic ability deceases when cells are condensed (volume fraction >0.01). However, the cell density is smaller than this critical value (volume fraction<0.01).

Additionally, the paper could better emphasize the new results and separate them from the confirmations of previous results.

In the revised version, we addressed 2 new findings:

1) The individual drift velocity decreases from back to front of the bacterial migration group, which makes the chemotactic migration wave a pushed wave.

2) Cells of diversed phenotypes follows the same reversion behavior, ie. drift faster in the back and slower in the front, but with ordered mean positions, to achieve the ordered pattern in the migration group.

Reviewer #2 (Public Review):

The manuscript by Bai et al. explores the single-cell motility dynamics within a chemotactic soliton wave in E. coli. They tracked individual cells and measured their trajectory speed and orientation distributions behind and ahead of the wave. They showed cells behind the wave were moving in a more directed fashion towards the center of the wave compared to cells ahead of the wave. This behavior explains the stability of group migration, as confirmed by numerical simulations.

I do not recommend this manuscript for publication in eLife since it basically reproduces and deepens previous published works. In particular, Saragosti et al (2011) already provided exactly what the authors claim to do here : "How individuals with phenotypic and behavioral variations manage to maintain the consistent group performance and determine their relative positions in the group is still a mystery." (Line 75-77) (See the last sentences from Saragosti et al : "This modulation of the reorientations significantly improves the efficiency of the collective migration. Moreover, these two quantities are spatially modulated along the concentration profile. We recover quantitatively these microscopic and macroscopic observations with a dedicated kinetic model.")

Saragosti et al.talks about the modulation of reorientation angle of bacteria along directions. It is not equal to the spatial modulation of drift velocities along space. They claim that cells moving along the gradient direction reorient less during a tumble than cells moving against the gradient. This phenomenon increases the migration efficiency of the group. Here, in our paper, we claim that the drift velocity of bacteria is spatially modulated, where cells on the back drifts faster while the cells in the front drift slower. This phenomenon is important because it makes the chemotactic migration front a pushed wave, that helps the group to keep diversed phenotypes.

Although Saragosti et al. Have also suggested spatial modulation of bias in run length to explain the coherency of the migration group. But they did not quantify such bias nor did they explain the causes and consequences of the spatial modulation. More over, Their model, consisting their proposed mechanism of directional persistence, can not explain their observed phenomenon of the decreasing bias of run length (see their figure 4A and C).In this circumstance, we can’t agree that they already proofed how cells with diversed phenotype to maintain coherent group.

Moreover, they did not talk about diversities in the group.

What is novel here is the titration of the behavior with chemo-receptor abundance, but I believe the scope is not wide enough for publication in eLife. I suggest the authors to submit in a more specialized journal.

The titration of the chemo-receptor abundance of bacteria serves as a tool to explain how diverse individuals manage to form the ordered patterns in a group. This question worth several discussion because diversity is known as an important feature to keep a group to survive. The ordered pattern was found the key for a migrating group to keep the diversity while performing consistent migration speed. In this paper we successfully explained how individuals performing biased random walk are able to form ordered structure.

Reviewer #3 (Public Review):

The authors present a study on the collective behaviour of E.coli during migration in a self-generated gradient. Taking into account phenotypic variation within a biological population, they performed experiments and complemented the study with a predictive model used for simulation to understand how bacteria can move as a group and how the individual bacterium defines its own position within the group.

They observed experimentally that phenotype variation within the bacterial population causes a spatial distribution within the chemotactic band that is not continuous but formed by subpopulations with specific properties such as run length, run duration, angular distribution of trajectories, drift velocity. They attribute this behaviour to the chemotaxis ability, which varies between phenotypes and defines a potential well that anchors each bacterium in its own group. This was proven by the subdiffusive dynamics of the bacteria in each subgroup. Many cases were studied in the experiments and the authors present many controls to clearly demonstrate their hypothesis.

These are interesting results that prove how a discretised distribution can produce continuous collective behaviour. It presents also an interesting example in the field of active matter about collective behaviour on a large scale that is generated by a different behaviour of individuals on a much smaller scale. However, it is not clear how the subpopulations can be held together in the group.

The decreasing chemo-attractant gradient makes the migration wavefront a pushed wavefront. So that the balanced position of the subpopulation with larger chemotactic ability is located in the front where the gradient is small. So that diverse phenotypes form ordered pattern to achieve identical migration speed on their balanced positions. This discussion was added in the revised text (see line 268-277).

Moreover, a link between bacterial dynamics and the biological necessary mechanism is not clear.

The bacterial individual dynamics is controlled by the bacterial chemotaxis pathway, which is clear according to previous studies. Basically, the biased random motion was controlled by alternating expected run length through a temporal comparison mechanism between received chemo-attractant concentrations.(Jiang et al. 2010 Plos Comp. Biol.)

They formulate a theoretical description based on the classical Keller-Segel model. Langevin dynamics was used to describe bacterial activity in terms of drift velocity for simulation, which agrees very well with experimental observations.

One can appreciate the interesting results of the study describing Ecoli chemotaxis as a mean-reversion process with an associated potential, but it is not clear to what extent the results can be generalised to all bacteria or rather relate to the strain the authors investigated.

The mean reversion process is a result of decreasing drift velocity (or a pushed wave). Although our study focuses on bacterail chemotaxis migration, but the ordering mechanism of diversed phenotypes follows a OU type model, which is not limited to bacterial chemotaxis. In this case, we argue that the ordering mechanism that we proposed is universal to all active particles that generate signals as a global cue of collective motion.

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:

The manuscript “A computationally designed fluorescent biosensor for D-serine" by Vongsouthi et al. reports the engineering of a fluorescent biosensor for D-serine using the D-alanine-specific solute-binding protein from Salmonella enterica (DalS) as a template. The authors engineer a DalS construct that has the enhanced cyan fluorescent protein (ECFP) and the Venus fluorescent protein (Venus) as terminal fusions, which serve as donor and acceptor fluorophores in resonance energy transfer (FRET) experiments. The reporters should monitor a conformational change induced by solute binding through a change of the FRET signal. The authors combine homology-guided rational protein engineering, in-silico ligand docking and computationally guided, stabilizing mutagenesis to transform DalS into a D-serine-specific biosensor applying iterative mutagenesis experiments. Functionality and solute affinity of modified DalS is probed using FRET assays. Vongsouthi et al. assess the applicability of the finally generated D-serine selective biosensor (D-SerFS) in-situ and in-vivo using fluorescence microscopy.

Ionotropic glutamate receptors are ligand-gated ion channels that are importantly involved in brain development, learning, memory and disease. D-serine is a co-agonist of ionotropic glutamate receptors of the NMDA subtype. The modulation of NMDA signalling in the central nervous system through D-serine is hardly understood. Optical biosensors that can detect D-serine are lacking and the development of such sensors, as proposed in the present study, is an important target in biomedical research.

The manuscript is well written and the data are clearly presented and discussed. The authors appear to have succeeded in the development of D-serine-selective fluorescent biosensor. But some questions arose concerning experimental design. Moreover, not all conclusions are fully supported by the data presented. I have the following comments.

1) In the homology-guided design two residues in the binding site were mutated to the ones of the D-serine specific homologue NR1 (i.e. F117L and A147S), which lead to a significant increase of affinity to D-serine, as desired. The third residue, however, was mutated to glutamine (Y148Q) instead of the homologous valine (V), which resulted in a substantial loss of affinity to D-serine (Table 1). This "bad" mutation was carried through in consecutive optimization steps. Did the authors also try the homologous Y148V mutation? On page 5 the authors argue that Q instead of V would increase the size of the side chain pocket. But the opposite is true: the side chain of Q is more bulky than the one of V, which may explain the dramatic loss of affinity to D-serine. Mutation Y148V may be beneficial.

Yes, we have previously tested the mutation of position 148 to valine (V). We have now included this data in the paper as Supplementary Information Figure 1 (below). The fluorescence titration showed that the 148V variant displayed poor D-serine specificity compared to Q148 at the same position (the sequence background of the variant was F117L/A147S/D216E/A76D. Thus, Q was superior to V at this position and V was not taken forward for further engineering. In the text, we meant that Q would increase the size of the side chain pocket relative to the wild-type amino acid, Y. We can see that this is unclear and have updated this sentence.

Supplementary Figure 1. Dose-response curves for F117L/A147S/Y148V/D216E/A76D (LSVED) with glycine, D-alanine and D-serine. Values are the (475 nm/530 nm) fluorescence ratio as a percentage of the same ratio for the apo sensor. No significant change is detected in response to glycine. The KD for D-alanine and D-serine are estimated to be > 4000 mM based on fitting curves with the following equation:

2) Stabilities of constructs were estimated from melting temperatures (Tm) measured using thermal denaturation probed using the FRET signal of ECFP/Venus fusions. I am not sure if this methodology is appropriate to determine thermal stabilities of DalS and mutants thereof. Thermal unfolding of the fluorescence labels ECFP and Venus and their intrinsic, supposedly strongly temperature-dependent fluorescence emission intensities will interfere. A deconvolution of signals will be difficult. It would be helpful to see raw data from these measurements. All stabilities are reported in terms of deltaTm. What is the absolute Tm of the reference protein DalS? How does the thermal stability of DalS compare to thermal stabilities of ECFP and Venus? A more reliable probe for thermal stability would be the far-UV circular dichroism (CD) spectroscopic signal of DalS without fusions. DalS is a largely helical domain and will show a strong CD signal.

We agree that raw data for the thermal denaturation experiments should be shown and have included this in the supporting information of an updated manuscript (Supplementary Data Figure 7). The data plots ECFP/Venus fluorescence ratio against temperature. When the temperature is increased from 20 to 90 °C, we observe two transitions in the ECFP/Venus fluorescence ratio. The fluorescent proteins are more thermostable than the DalS binding protein, and that temperature transition does not vary (~90 °C); thus, the first transition corresponds to the unfolding of the binding protein and the second transition to the unfolding or loss of fluorescence from the fluorescent proteins. This is an appropriate method for characterising the thermostability of the binding protein in the sensor for two main reasons. Firstly, the calculated melting temperature from the first sigmoidal transition changes upon mutation to the binding protein in a predictable way (e.g. mutations to the binding site/protein core are destabilising), while the second transition occurs consistently at ~ 90 °C. This supports that the first transition corresponds to the unfolding of the binding protein. Secondly, characterising the stability of the binding protein in the context of the full sensor is more relevant to the end-application. Excising the binding domain and testing that in isolation would results in data that are not directly relevant to the sensor. The absolute thermostabilities for all variants can be found in Table 1 of the manuscript.

Supplementary Figure 7. The (475 nm/530 nm) fluorescence ratio as a function of increasing temperature (20 – 90 °C) for key variants in the engineering trajectory of D-serFS. Values are normalised as a percentage of the same ratio for the sensor at 20 °C and are represented as mean ± s.e.m. (n = 3). The first sigmoidal transition in the data changes upon mutation to the binding protein while the second transition begins at ~ 90 °C for all variants. The second transition is not observed in full as the upper temperature limit for the experiment is 90 °C.

3) The final construct D-SerFS has a dynamic range of only 7%, which is a low value. It seems that the FRET signal change caused by ligand binding to the construct is weak. Is it sufficient to reliably measure D-serine levels in-situ and in-vivo?

First, we have modified the sensor, which now has a dynamic range of 14.7% (Figure 5, below). The magnitude of the change is reasonable for this sensor class; they function with relative low dynamic range because they are ratiometric sensors, i.e. they are accurate even with low dynamic range because of their ratiometric property. For example, the Gly-sensor GlyFS published in 2018 (Nature Chem. Biol.) has one of the highest dynamic ranges in this sensor class of only ~28%. The Glu sensor described by Okumuto et al., (2005) (PNAS, 102, 8740) has a dynamic range of ~9%. So, the FRET change is not a low value for ratiometric sensors of this class (which have been used very effectively for over a decade). Most importantly, the data from experiments with biological tissue and in vivo (Fig. 6) demonstrate a detectable (and statistically significant) response to changes in D-serine concentration in tissue.

Figure 5. Characterization of full-length D-serFS. (A) Schematic showing the ECFP (blue), D-serFS binding protein (D-serFS BP; grey) and Venus (yellow) domains in D-serFS. The C-terminal residues of the Venus fluorescent protein sequence are labelled, showing the truncated (top) and full-length (bottom) C-terminal sequences. The underlined amino acids in truncated D-serFS represent residues introduced from the backbone vector sequence during cloning. Represents the STOP codon. (B) Sigmoidal dose response curves for truncated and full-length D-serFS with D-serine (n = 3). Values are the (475 nm/530 nm) fluorescence ratio as a percentage of the same ratio for the apo sensor. (C) Binding affinities (M) determined by fluorescence titration of truncated and full-length D-serFS, for glycine, D-alanine and D-serine (n = 3).*

In Figure 5H in-vivo signal changes show large errors and the signal of the positive sample is hardly above error compared to the signal of the control.

We have removed the in vivo data. Regardless, the comment is incorrect. Statistical analysis confirms that there is no significant change in the control (P = 0.08411), whereas the change for the sample with D-serine was significant to P = 0.00998.

“H) ECFP/Venus ratio recorded in vivo in control recordings (left panel, baseline recording first, control recording after 10 minutes; paired two-sided Student’s t-test vs. baseline, t(6) = -2.07,P = 0.08411; n = 6 independent experiments) and during D-serine application (right panel, baseline recording first, second recording after D-serine injection, 1 mM; paired two-sided Student’s t-test vs. baseline, t(3) = -5.85,P = 0.00998; n = 4 independent experiments). Values are mean +- s.e.m. throughout. **P < 0.01.”

Figure 5G is unclear. What does the fluorescence image show?

We have removed the in-vivo data from the manuscript. However, Figure 6 in the original manuscript shows a schematic of how the sensor is applied to the brain for in-vivo experiments (biotin injection, followed by sensor injection and then imaging). The fluorescence image shows the detected Venus fluorescence following pressure loading of the sensor into the brain.

Work presented in this manuscript that assesses functionality and applicability of the developed sensor in-situ and in-vivo is limited compared to the work showing its design. For example, control experiments showing FRET signal changes of the wild-type ECFP-DalS-Venus construct in comparison to the designed D-SerFS would be helpful to assess the outcome.

Indeed, the in situ and in vivo work was never the focus of the study, which is already a large paper. To avoid confusion, the in vivo work is now omitted and the in situ work is present to show proof, in principle, that the sensor can be used to image D-serine. We reiterate – this is a protein engineering paper, not a neuroscience paper.

4) The FRET spectra shown in Supplementary Figure 2, which exemplify the measurement of fluorescence ratios of ECFP/Venus, are confusing. I cannot see a significant change of FRET upon application of ligand. The ratios of the peak fluorescence intensities of ECFP and Venus (scanned from the data shown in Supplementary Figure 2) are the same for apo states and the ligand-saturated states. Instead what happens is that fluorescence emission intensities of both the donor and the acceptor bands are reduced upon application of ligand.

We thank the reviewer for bringing this to our attention. The spectra were not normalised to account for the effect of dilution when saturating with ligand, giving rise to an observed decrease in emission intensity from both ECFP and Venus. We can also see how the figure is hard to interpret when both variants are displayed on the same axes, so we have separated them in an updated figure shown below and normalised the data as a percentage of the maximum emission intensity from ECFP at 475 nm. This has been changed in the supporting information of an updated manuscript. Hopefully it is now clear that there is a ratiometric change upon addition of ligand.

Figure 3. Emission spectra (450 – 550 nm) of (A) LSQED and (B) LSQED-T197Y (LSQEDY) upon excitation of ECFP (lexc = 433 nm), normalised to the maximum emission intensity from ECFP (475 nm). For all sensor variants, the FRET efficiency decreases in response to saturation with D-serine (A, B; orange), leading to decreased emission from Venus (530 nm) relative to ECFP (475 nm). When comparing the apo states of LSQED and LSQEDY (A, B; dark green), it can be seen that the T197Y mutation results in a decreased Venus emission (lower FRET efficiency). This suggests a shift in the apo population of the sensor towards the spectral properties of the saturated, closed state and explains the decreased dynamic range of LSQEDY compared to LSQED. Values are mean ± s.e.m (n = 3).

Reviewer #2:

The authors describe the development and use of a D-Serine sensor based on a periplasmic ligand binding protein (DalS) from Salmonella enterica in conjunction with a FRET readout between enhanced cyan fluorescent protein and Venus fluorescent protein. They rationally identify point mutations in the binding pocket that make the binding protein somewhat more selective for D-serine over glycine and D-alanine. Ligand docking into the binding site, as well as algorithms for increasing the stability, identified further mutants with higher thermostability and higher affinity for D-serine. The combined computational efforts lead to a sensor for D-serine with higher affinity for D-serine (Kd = ~ 7 µM), but also showed affinity for the native D-alanine (Kd = ~ 13 uM) and glycine (Kd = ~40 uM). Molecular simulations were then used to explain how remote mutations identified in the thermostability screen could lead to the observed alteration of ligand affinity. Finally, the D-SerFS was tested in 2P-imaging in hippocampal slices and in anesthetized mice using biotin-straptavidin to anchor exogenously applied purified protein sensor to the brain tissue and pipetting on saturating concentrations of D-serine ligand.

Although presented as the development of a sensor for biology, this work primarily focuses on the application of existing protein engineering techniques to alter the ligand affinity and specificity of a ligand-binding protein domain. The authors are somewhat successful in improving specificity for the desired ligand, but much context is lacking. For any such engineering effort, the end goals should be laid out as explicitly as possible. What sorts of biological signals do they desire to measure? On what length scale? On what time scale? What is known about the concentrations of the analyte and potential competing factors in the tissue? Since the authors do not demonstrate the imaging of any physiological signals with their sensor and do not discuss in detail the nature of the signals they aim to see, the reader is unable to evaluate what effect (if any) all of their protein engineering work had on their progress toward the goal of imaging D-serine signals in tissue.

As a paper describing a combination of protein engineering approaches to alter the ligand affinity and specificity of one protein, it is a relatively complete work. In its current form trying to present a new fluorescent biosensor for imaging biology it is strongly lacking. I would suggest the authors rework the story to exclusively focus on the protein engineering or continue to work on the sensor/imaging/etc until they are able to use it to image some biology.

Additional Major Points:

1) There is no discussion of why the authors chose to use non-specific chemical labeling of the tissue with NHS-biotin to anchor their sensor vs. genetic techniques to get cell-type specific expression and localization. There is no high-resolution imaging demonstrating that the sensor is localized where they intended.

We use non-specific chemical labelling for proof-of-concept experiments that show the sensor can respond to changes in D-serine concentration in the extracellular environment of brain tissue. Cell-type specific expression of the sensor is possible based on our previous development of a similar sensor for glycine (Zhang et al., 2018; doi: https://doi.org/10.1038/s41589-018-0108-2) where the sensor was expressed by HEK293 cells and neurons, and targeted to the membrane. However, this is beyond the scope of this manuscript. Figure 5G of the original manuscript shows that the sensor (identified by Venus fluorescence) is localized to the area where D-serFS is pressure-loaded into the brain.

2) Why does the fluorescence of both the CFP and they YFP decrease upon addition of ligand (see e.g. Supplementary Figure 2)? Were these samples at the same concentration? Is this really a FRET sensor or more of an intensiometric sensor? Is this also true with 2P excitation? How does the Venus fluorescence change when Venus is excited directly? Perhaps fluorescence lifetime measurements could help inform what is happening.

Please see response to major comments from reviewer #1 and Figure 3. We hope this clarifies that the sensor is ratiometric. The sensor behaves similarly under two-photon excitation (2PE) as shown in Figure 5A.

3) How reproducible are the spectral differences between LSQED and LSQED-T197Y? Only one trace for each is shown in Supplementary Figure 2 and the differences are very small, but the authors use these data to draw conclusions about the protein open-closed equilibrium.

We have updated this to show data points representing the mean ± s.e.m (n = 3).

4) The first three mutations described are arrived upon by aligning DalS (which is more specific for D-Ala) with the NMDA receptor (which binds D-Ser). The authors then mutate two of the ligand pocket positions of DalS to the same amino acid found in NMDAR, but mutate the third position to glutamine instead of valine. I really can't understand why they don't even test Y148V if their goal is a sensor that hopefully detects D-Ser similar to the native NMDAR. I'm sure most readers will have the same confusion.

Please see response to major comments from reviewer #1. Additionally, while the NR1 binding domain of the NMDAR was used a structural guide for rational design of the DalS binding site, the high affinity of the NMDAR for both D-serine and glycine was not desirable in a D-serine-specific sensor.

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):

In this manuscript, Abdellatef et al. describe the reconstitution of axonemal bending using polymerized microtubules (MTs), purified outer-arm dyneins, and synthesized DNA origami. Specifically, the authors purified axonemal dyneins from Chlamydomonas flagella and combined the purified motors with MTs polymerized from purified brain tubulin. Using electron microscopy, the authors demonstrate that patches of dynein motors of the same orientation at both MT ends (i.e., with their tails bound to the same MT) result in pairs of MTs of parallel alignment, while groups of dynein motors of opposite orientation at both MT ends (i.e., with the tails of the dynein motors of both groups bound to different MTs) result in pairs of MTs with anti-parallel alignment. The authors then show that the dynein motors can slide MTs apart following photolysis of caged ATP, and using optical tweezers, demonstrate active force generation of up to ~30 pN. Finally, the authors show that pairs of anti-parallel MTs exhibit bidirectional motion on the scale of ~50-100 nm when both MTs are cross-linked using DNA origami. The findings should be of interest for the cytoskeletal cell and biophysics communities.

We thank the reviewer for these comments.

We might be misunderstanding this reviewer’s comment, but the complexes with both parallel and anti-parallel MTs had dynein molecules with their tails bound to two different MTs in most cases, as illustrated in Fig.2 – suppl.1. The two groups of dyneins produce opposing forces in a complex with parallel MTs, and majority of our complexes had parallel arrangement of the MTs. To clarify the point, we have modified the Abstract:

“Electron microscopy (EM) showed pairs of parallel MTs crossbridged by patches of regularly arranged dynein molecules bound in two different orientations depending on which of the MTs their tails bind to. The oppositely oriented dyneins are expected to produce opposing forces when the pair of MTs have the same polarity.”

Reviewer #2 (Public Review):

Motile cilia generate rhythmic beating or rotational motion to drive cells or produce extracellular fluid flow. Cilia is made of nine microtubule doublets forming a spoke-like structure and it is known that dynein motor proteins, which connects adjacent microtubule doublet, are the driving force of ciliary motion. However the molecular mechanism to generate motion is still unclear. The authors proved that a pair of microtubules stably linked by DNA-origami and driven by outer dynein arms (ODA) causes beating motion. They employed in vitro motility assay and negative stain TEM to characterize this complex. They demonstrated stable linking of microtubules and ODAs anchored on the both microtubules are essential for oscillatory motion and bending of the microtubules.

Strength

This is an interesting work, addressing an important question in the motile cilia community: what is the minimum system to generate a beating motion? It is an established fact that dynein power stroke on the microtubule doublet is the driving force of the beating motion. It was also known that the radial spoke and the central pair are essential for ciliary motion under the physiological condition, but cilia without radial spokes and the central pair can beat under some special conditions (Yagi and Kamiya, 2000). Therefore in the mechanistic point of view, they are not prerequisite. It is generally thought that fixed connection between adjacent microtubules by nexin converts sliding motion of dyneins to bending, but it was never experimentally investigated. Here the authors successfully enabled a simple system of nexin-like inter-microtubule linkage using DNA origami technique to generate oscillatory and beating motions. This enables an interesting system where ODAs form groups, anchored on two microtubules, orienting oppositely and therefore cause tag-of-war type force generation. The authors demonstrated this system under constraints by DNA origami generates oscillatory and beating motions.

The authors carefully coordinated the experiments to demonstrate oscillations using optical tweezers and sophisticated data analysis (Fourier analysis and a step-finding algorithm). They also proved, using negative stain EM, that this system contains two groups of ODAs forming arrays with opposite polarity on the parallel microtubules. The manuscript is carefully organized with impressive movies. Geometrical and motility analyses of individual ODAs used for statistics are provided in the supplementary source files. They appropriately cited similar past works from Kamiya and Shingyoji groups (they employed systems closer to the physiological axoneme to reproduce beating) and clarify the differences from this study.

We thank the reviewer for these comments.

Weakness

The authors claim this system mimics two pairs of doublets at the opposite sites from 9+2 cilia structure by having two groups of ODAs between two microtubules facing opposite directions within the pair. It is not exactly the case. In the real axoneme, ODA makes continuous array along the entire length of doublets, which means at any point there are ODAs facing opposite directions. In their system, opposite ODAs cannot exist at the same point (therefore the scheme of Dynein-MT complex of Fig.1B is slightly misleading).

Actually, opposite ODAs can exist at the same point in our system as well, and previous work using much higher concentration of dyneins (e.g, Oda et al., J. Cell biol., 2007) showed two continuous arrays of dynein molecules between a pair of microtubules. To observe the structures of individual dynein molecules we used low concentrations of dynein and searched for the areas where dynein could be observed without superposition, but there were some areas where opposite dyneins existed at the same point.

We realize that we did not clearly explain this issue, so we have revised the text accordingly.

In the 1st paragraph of Results: “In the dynein-MT complexes prepared with high concentrations of dynein, a pair of MTs in bundles are crossbridged by two continuous arrays of dynein, so that superposition of two rows of dynein molecules is observed in EM images (Haimo et al., 1979; Oda et al., 2007). On the other hand, when a low concentration of the dynein preparation (6.25–12.5 µg/ml (corresponding to ~3-6 nM outer-arm dynein)) was mixed with 20-25 µg/ml MTs (200-250 nM tubulin dimers), the MTs were only partially decorated with dynein, so that we were able to observe single layers of crossbridges without superposition in many regions.” Legend of Fig. 1(C): “Note that the geometry of dyneins in the dynein-MT complex shown in (B) mimics that of a combination of the dyneins on two opposite sides of the axoneme (cyan boxes), although the dynein arrays in (B) are not continuous.”

If they want to project their result to the ciliary beating model, more insight/explanation would be necessary. For example, arrays of dyneins at certain positions within the long array along one doublet are activated and generate force, while dyneins at different positions are activated on another doublet at the opposite site of the axoneme. This makes the distribution of dyneins and their orientations similar to the system described in this work. Such a localized activation, shown in physiological cilia by Ishikawa and Nicastro groups, may require other regulatory proteins.

We agree that the distributions of activated dyneins in 3D are extremely important in understanding ciliary beating, and that other regulatory proteins would be required to coordinate activation in different places in an axoneme. However, the main goal of this manuscript is to show the minimal components for oscillatory movements, and we feel that discussing the distributions of activated dyneins along the length of the MTs would be too complicated and beyond the scope of this study.

They attempted to reveal conformational change of ODAs induced by power stroke using negative stain EM images, which is less convincing compared to the past cryo-ET works (Ishikawa, Nicastro, Pigino groups) and negative stain EM of sea urchin outer dyneins (Hirose group), where the tail and head parts were clearly defined from the 3D map or 2D averages of two-dynein ODAs. Probably three heavy chains and associated proteins hinder detailed visualization of the tail structure. Because of this, Fig.2C is not clear enough to prove conformational change of ODA. This reviewer imagines refined subaverage (probably with larger datasets) is necessary.

As the reviewer suggests, one of the reasons for less clear averaged images compared to the past images of sea urchin ODA is the three-headed structure of Chlamydomonas ODA. Another and perhaps the bigger reason is the difficulty of obtaining clear images of dynein molecules bound between 2 MTs by negative stain EM: the stain accumulates between MTs that are ~25 nm in diameter and obscures the features of smaller structures. We used cryo-EM with uranyl acetate staining instead of negative staining for the images of sea urchin ODA-MT complexes we previously published (Ueno et al., 2008) in order to visualize dynein stalks. We agree with the reviewer that future work with larger datasets and by cryo-ET is necessary for revealing structural differences.

That having been said, we did not mean to prove structural changes, but rather intended to show that our observation suggests structural changes and thus this system is useful for analyzing structural changes in future. In the revised manuscript, we have extensively modified the parts of the paper discussing structural changes (Please see our response to the next comment).

It is not clear, from the inset of Fig.2 supplement3, how to define the end of the tail for the length measurement, which is the basis for the authors to claim conformational change (Line263-265). The appearance of the tail would be altered, seen from even slightly different view angles. Comparison with 2D projection from apo- and nucleotide-bound 3-headed ODA structures from EM databank will help.

We agree with the reviewer that difference in the viewing angle affects the apparent length of a dynein molecule, although the 2 MTs crossbridged by dyneins lie on the carbon membrane and thus the variation in the viewing angle is expected to be relatively small. To examine how much the apparent length is affected by the view angle, we calculated 2D-projected images of the cryo-ET structures of Chlamydomonas axoneme (emd_1696 and emd_1697; Movassagh et al., 2010) with different view angles, and measured the apparent length of the dynein molecule using the same method we used for our negative-stain images (Author response image 1). As shown in the plot, the effect of view angles on the apparent lengths is smaller than the difference between the two nucleotide states in the range of 40 degrees measured here. Thus, we think that the length difference shown in Fig.2-suppl.4 reflects a real structural difference between no-ATP and ATP states. In addition, it would be reasonable to think that distributions of the view angles in the negative stain images are similar for both absence and presence of ATP, again supporting the conclusion.

Nevertheless, since we agree with the reviewer that we cannot measure the precise length of the molecule using these 2D images, we have revised the corresponding parts of the manuscript, adding description about the effect of view angles on the measured length in the manuscript.

Author response image 1. Effects of viewing angles on apparent length. (A) and (B) 2D-projected images of cryo-electron tomograms of Chlamydomonas outer arm dynein in an axoneme (Movassagh et al., 2010) viewed from different angles. (C) apparent length of the dynein molecule measured in 2D-projected images.

In this manuscript, we discuss two structural changes: 1) a difference in the dynein length between no-nucleotide and +ATP states (Fig.2-suppl.4), and 2) possible structural differences in the arrangement of the dynein heads (Fig.2-suppl.3). Although we realize that extensive analysis using cryo-ET is necessary for revealing the second structural change, we attempted to compare the structures of oppositely oriented dyneins, hoping that it would lead to future research. In the revised manuscript, we have added 2D projection images of emd_1696 and emd_1697 in Fig.2-suppl.3, so that the readers can compare them with our negative stain images. We had an impression that some of our 2D images in the presence of ATP resembled the cryo-ET structure with ADP.Vi, whereas some others appeared to be closer to the no-nucleotide cryo-ET structure. We have also attempted to calculate cross-correlations, but difficulties in removing the effect of MTs sometimes overlapped with a part of dynein, adjusting the magnifications and contrast of different images prevented us from obtaining reliable results.

To address this and the previous comments, we have extensively modified the section titled ‘Structures of dynein in the dynein-MT-DNA-origami complex’.

In Fig.5B (where the oscillation occurs), the microtubule was once driven >150nm unidirectionally and went back to the original position, before oscillation starts. Is it always the case that relatively long unidirectional motion and return precede oscillation? In Fig.7B, where the authors claim no oscillation happened, only one unidirectional motion was shown. Did oscillation not happen after MT returned to the original position?

Long unidirectional movement of ~150 nm was sometimes observed, but not necessarily before the start of oscillation. For example, in Figure 5 – figure supplement 1A, oscillation started soon after the UV flash, and then unidirectional movement occurred.

With the dynein-MT complex in which dyneins are unidirectionally aligned (Fig.7B, Fig.7-suppl.2), the MTs kept moving and escaped from the trap or just stopped moving probably due to depletion of ATP, so we did not see a MT returning to the original position.

Line284-290: More characterization of bending motion will be necessary (and should be possible). How high frequency is it? Do they confirm that other systems (either without DNA-origami or without ODAs arraying oppositely) cannot generate repetitive beating?

The frequencies of the bending motions measured from the movies in Fig.8 and Fig.8-suppl.1 were 0.6 – 1 Hz, and the motions were rather irregular. Even if there were complexes bending at high frequencies, it would not have been possible to detect them due to the low time resolution of these fluorescence microscopy experiments (~0.1 s). Future studies at a higher time resolution will be necessary for further characterization of bending motions.

To observe bending motions, the dynein-MT complex should be fixed to the glass or a bead at one part of the complex while the other end is free in solution. With the dynein-MT-DNA-origami complexes, we looked for such complexes and found some showing bending motions as in Fig. 8. To answer the reviewer’s question asking if we saw repetitive bending in other systems, we checked the movies of the complexes without DNA-origami or without ODAs arraying oppositely but did not notice any repetitive bending motions. However, future studies using the system with a higher temporal resolution and perhaps with an improved method for attaching the complex would be necessary in these cases as well.

Author Response

Reviewer #1 (Public Review):

Overall, this study is well designed with convincing experimental data. The following critiques should be considered:

1) It is important to examine whether the phenotype of METTL18 KO is mediated through change with RPL3 methylation. The functional link between METTL18 and RPL3 methylation on regulating translation elongation need to be examined in details.

We truly thank the reviewer for the suggestion. Accordingly, we set up experiments combined with hybrid in vitro translation (Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) and the Renilla–firefly luciferase fusion reporter system (Kisly et al. NAR 2021) (see Figure 5A).

To test the impact of RPL3 methylation on translation directly, we purified ribosomes from METTL18 KO cells or naïve HEK293T cells supplemented with ribosome-depleted rabbit reticulocyte lysate (RRL) and then conducted an in vitro translation assay (i.e., hybrid translation, Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) (see figure above and Figure 5A). Indeed, we observed that removal of the ribosomes from RRL decreased protein synthesis in vitro and that the addition of ribosomes from HEK293T cells efficiently recovered the activity (see Figure 5 — figure supplement 1A).

To test the effect on Tyr codon elongation, we harnessed the fusion of Renilla and firefly luciferases; this system allows us to detect the delay/promotion of downstream firefly luciferase synthesis compared to upstream Renilla luciferase and thus to focus on elongation affected by the sequence inserted between the two luciferases (Kisly et al. NAR 2021) (see figure above and Figure 5A). For better detection of the effects on Tyr codons, we used the repeat of the codon (×39, the number was due to cloning constraints in our hands). We note that the insertion of Tyr codon repeats reduced the elongation rate (or processivity), as we observed a reduced slope of downstream Fluc synthesis (see Figure 5 — figure supplement 1B).

Using this setup, we observed that, compared to ribosomes from naïve cells, RPL3 methylation-deficient ribosomes led to faster elongation at Tyr repeats (see Figure 5B). These data, which are directly reflected by the ribosomes possessing unmethylated RPL3, provided solid evidence of a link between RPL3 methylation and translation elongation at Tyr codons.

2) The obvious discrepancy between the recent NAR an this study lies in the ribosomal profiling results (such as Fig.S5). The cell line specific regulation between HAP1 (previously used in NAR) vs 293T cell used here ( in this study) needs to be explored. For example, would METLL18 KO in HAP1 cells cause polysome profiling difference in this study? Some of negative findings in this study (such as Fig.S3B, Fig.S5A) would need some kind of positive control to make sure that the assay condition would be working.

According to the reviewer’s suggestion, we conducted polysome profiling of the HAP1 cells with METTL18 knockout. For this assay, we used the same cell line (HAP1 METTL18 KO, 2-nt del.) as in the earlier NAR paper. As shown in Figure 9 — figure supplement 2A and 2B, we observed reduced polysomes in this cell line, as observed in the NAR paper.

We did not find the abundance of 40S and 60S by assessing the rRNAs and the complex mass in the sucrose gradient (see Figure 9 — figure supplement 2C-E) by METTL18 KO in HAP1 cells. This observation was again consistent with earlier reports.

Overall, our experiments in sucrose density gradient (polysome and 40S/60S ratio) were congruent with NAR paper. A difference from our finding in HEK293T cells was the limited effect on polysome formation by METTL18 deletion (Figure 4 — figure supplement 1A and 1B). To further provide a careful control for this observation, we induced a 60S biogenesis delay, as requested by the Reviewer. Here, we treated cells with siRNA targeting RPL17, which is needed for proper 60S assembly (Wang et al. RNA 2015). The quantification of SDG showed a reduction of 60S (see figure below and Figure 3 — figure supplement 1D-F) and polysomes (see Figure 4 — figure supplement 1C and 1D), highlighting the weaker effects of METTL18 depletion on 60S and polysome formation in HEK293T cells. We note that all the sucrose density gradient experiments were repeated 3 times, quantified, and statistically tested.

To further assess the difference between our data and those in the earlier NAR paper, we also performed ribosome profiling on 3 independent KO lines in HAP1 cells, including the one used in the NAR paper (METTL18 KO, 2-nt del.). Indeed, all METTL18 KO HAP1 cells showed a reduction in footprints on Tyr codons, as observed in HEK293 cells (see Figure 4H), and thus, there was a consistent effect of RPL3 methylation on elongation irrespective of the cell type. On the other hand, we could not find such a trend (see figure below) by reanalysis of the published data (Małecki et al. NAR 2021).

Thus far, we could not find the origin of the difference in ribosome profiling compared to the earlier paper. Culture conditions or other conditions may affect the data. Given that, we amended the discussion to cover the potential of context/situation-dependent effects on RPL3 methylation.

3) For loss-of-function studies of METLL18, it will be beneficial to have a second sgRNA to KO METLL18 to solidify the conclusion.

We thank the reviewer for the constructive suggestion. Instead of screening additional METTL18 KO in HEK293T cells, we conducted additional ribosome profiling experiments in HAP1 cells with 3 independent KO lines. In addition to ensuring reproducibility, these experiments should assess whether our results are specific to the HEK293T cells that we mainly used. As mentioned above, even in the different cell lines, we observed faster elongation of the Tyr codon by METTL18 deficiency.

4) In addition to loss-of-function studies for METLL18, gain-of-function studies for METLL18 would be helpful for making this study more convincing.

Again, we thank the reviewer for the constructive suggestion. To address this issue, we conducted RiboTag-IP and subsequent ribosome profiling. Here, we expressed Cterminal FLAG-tagged RPL3 of its WT and His245Ala mutant, in which METTL18 could not add methylation (Figure 2A), in HEK293T cells, treated the lysate with RNase, immunoprecipitated FLAG-tagged ribosomes, and then prepared a ribosome profiling library (see figure below, left). This experiment assessed the translation driven by the tagged ribosomes. Indeed, we observed that, compared to the difference in Tyr codon elongation in METTL18 KO vs. naïve cells, His245Ala provided weaker impacts (see figure below, right). Given that METTL18 KO provides unmodified His, the enhanced Tyr elongation may be mediated by the bare His but not by Ala in that position. Since this point may be beyond the scope of this study, we omitted it from the manuscript. However, we are happy to add the data to the supplementary figures if requested.

Reviewer #3 (Public Review):

In this article, Matsuura-Suzuki et al provided strong evidence that the mammalian protein METTL18 methylates a histidine residue in the ribosomal protein RPL3 using a combination of Click chemistry, quantitative mass spectrometry, and in vitro methylation assays. They showed that METTL18 was associated with early sucrose gradient fractions prior to the 40S peak on a polysome profile and interpreted that as evidence that RPL3 is modified early in the 60S subunit biogenesis pathway. They performed cryo-EM of ribosomes from a METTL18-knockout strain, and show that the methyl group on the histidine present in published cryo-EM data was missing in their new cryo-EM structure. The missing methyl group gave minor changes in the residue conformation, in keeping with the minor effects observed on translation. They performed ribosome profiling to determine what is being translated efficiently in cells with and without METTL18, and found decreased enrichment of Tyrosine codons in the A site of ribosomes from cells lacking METTL18. They further showed that longer ribosome footprints corresponding to sequences within ribosomes that have already bound to A-site tRNA contained less Tyrosine codons in the A site when lacking METTL18. This suggests methylation normally slows down elongation after tRNA loading but prior to EF-2 dissociation. They hypothesize that this decreased rate affects protein folding and follow up with fluorescence microscopy to show that EGFP aggregated more readily in cells lacking METTL18, suggesting that translation elongation slow down mediated by METTL18 leads to enhanced folding. Finally, they performed SILAC on aggregated proteins to confirm that more tyrosine was incorporated into protein aggregates from cells lacking METTL18.

The article is interesting and uses a large number of different techniques to present evidence that histidine methylation of RPL3 leads to decreased elongation rates at Tyrosine codons, allowing time for effective protein folding.

We thank the reviewer for the positive comments.

I agree with the interpretation of the results, although I do have minor concerns:

1) The magnitude of each effect observed by ribosome profiling is very small, which is not unusual for ribosome modifications or methylation. Methylation seems to occur on all ribosomes in the cell since the modification is present in several cryo-EM structures. The authors suggest that the modification occurs during biogenesis prior to folding and being inaccessible to METTL18, so it is unlikely to be removed. For that reason, I do not think it is warranted to claim that this is an example of a ribosome code, or translation tuning. Those terms would indicate regulated modifications that come on and off of proteins, but the authors have not presented evidence that the activity is regulated (and don't really need to for this paper to be impactful).

We thank the reviewer for making this point, and we agree that the nuance of the wording may not fit our results. We amended the corresponding sentences to avoid using the terms “ribosome code” and “translation tuning” throughout the manuscript.

2) In Figure 4-supplement 1, it appears there are slightly more 80S less 60S in the METTL18 knockout with no change in 40S. It might be normal variability in this cell type, but quantitation of the peaks from 2 or more experiments is needed to make the claim that ribosome biogenesis is unaffected by METTL18 deletion. Likewise, the authors need to quantitate the area under the curve for 40S and 60S levels from several replicates and show an average -/+ error for figure 3, supplement 1 because that result is essential to claim that ribosome biogenesis is unaffected.

Accordingly, we repeated all the sucrose density gradient experiments 3 times, quantified the data, and statistically tested the results. Even in the quantification, we could not find a significant change in either the 40S or 60S levels by METTL18 deletion in HEK293T cells (see Figure 3 — figure supplement 1B and 1C).

Moreover, for the positive control of 60S biogenesis delay, we treated cells with siRNA targeting RPL17, which is needed for proper 60S assembly (Wang et al. RNA 2015). The quantification of SDG showed a reduction in 60S (see figure below and Figure 3 — figure supplement 1D-F) and polysomes (see Figure 4 — figure supplement 1C and 1D), highlighting the weaker effects of METTL18 depletion on 60S and polysome formation.

3) The effect of methylation could be any step after accommodation of tRNA in the A site and before dissociation of EF-2, including peptidyl transfer. More evidence is needed for claiming strongly that methylation slows translocation specifically. This could be followed up in vitro in a new study.

We truly thank the reviewer for the suggestion. Accordingly, we set up experiments combined with hybrid in vitro translation (Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) and the Renilla–firefly luciferase fusion reporter system (Kisly et al. NAR 2021) (see Figure 5A).

To test the impact of RPL3 methylation on translation directly, we purified ribosomes from METTL18 KO cells or naïve HEK293T cells supplemented with ribosome-depleted rabbit reticulocyte lysate (RRL) and then conducted an in vitro translation assay (i.e., hybrid translation, Panthu et al. Biochem J 2015 and Erales et al. PNAS 2017) (see figure above and Figure 5A). Indeed, we observed that removal of the ribosomes from RRL decreased protein synthesis in vitro and that the addition of ribosomes from HEK293T cells efficiently recovered the activity (see Figure 5 — figure supplement 1A).

To test the effect on Tyr codon elongation, we harnessed the fusion of Renilla and firefly luciferases; this system allows us to detect the delay/promotion of downstream firefly luciferase synthesis compared to upstream Renilla luciferase and thus to focus on elongation affected by the sequence inserted between the two luciferases (Kisly et al. NAR 2021) (see figure above and Figure 5A). For better detection of the effects on Tyr codons, we used the repeat of the codon (×39, the number was due to cloning constraints in our hands). We note that the insertion of Tyr codon repeats reduced the elongation rate (or processivity), as we observed a reduced slope of downstream Fluc synthesis (see Figure 5 — figure supplement 1B).

Using this setup, we observed that, compared to ribosomes from naïve cells, RPL3 methylation-deficient ribosomes led to faster elongation at Tyr repeats (see Figure 5B). These data, which are directly reflected by the ribosomes possessing unmethylated RPL3, provided solid evidence of a link between RPL3 methylation and translation elongation at Tyr codons.

Author Response

Reviewer #1 (Public Review):

Adefuin and colleagues examined the interaction between components of binary odor mixtures in odor responses in mice. The authors used two-photon calcium imaging from the soma and apical dendrites of mitral/tufted cells in the olfactory bulb. Odor responses were measured in various conditions: under anesthesia (ketamine/xylazine), while well-trained mice were engaged in an odor discrimination task, or disengaged. The authors first show that mixture components interacted sublinearly in a large fraction of mitral/tufted cells (46%; Fig. 6D) consistent with previous studies. However, when odor responses were measured in awake animals, very few mitral/tufted cells showed sublinear responses at soma (8-9%; Fig. 6D). Interestingly, sublinear interaction was evident in apical dendrites of mitral/tufted cells (45%). Whether mixture components are represented linearly or not in the olfactory system is an important question, related to the animal's ability to identify or segment mixture components. Somewhat contrary to previous studies, this study demonstrate largely linear interactions. Furthermore, this study compares various behavioral conditions. These results are important and of interest to those who study sensory systems. I have a few concerns regarding data analysis.

Thank you for your helpful review, and for recognising the relevance our work. We hope that the reviewer finds the our point-by-point responses satisfactory.

1) Non-linear interactions are detected by the activity showing a deviation from linearity greater than 2 standard deviations. Using this criterion, non-linear interactions might decrease if the trial-by-trial activity becomes more variable. This is concerning because the activity might be less variable in the anesthetized condition, and the reduction in sublinear interactions in awake conditions may be due to a general increase in response variability during awake. Can the authors exclude the possibility that the decrease in sublinear interactions is merely due to an increase in response variability in the awake conditions. This issue also applies to the comparison between apical dendrites versus soma; are the signals in apical dendrite less variable (maybe due to some averaging across dendrites from multiple cells; see the following point 5)?

Thank you for raising this valid point and for suggesting alternative analyses. We agree that the index we used previously is susceptible to noise, and not appropriate for comparing two datasets with different trial-by-trial variability. To quantify the deviation from linear sum more robustly, we now use the “Median fractional deviation”, which expresses a deviation from the linear sum as a fraction of predicted, linear sum - not normalised by the standard deviation – and take the median of the distribution from each field of view. As we describe in the revised Figure 4, this measure is more robust to noise. Notably, our finding that mixture summation is generally less sublinear in awake mice still stands for the early phase.

In the revised manuscript, we use the median fractional deviation whenever we compare linearity of summation across different conditions, which includes the comparison of anaesthetised vs. awake, behaving conditions (revised Fig. 4), comparison of dendrites vs. somata (revised Fig. 4-figure supplement 1), and comparisons of awake states (revised Fig. 6). This has given us, too, more confidence about our interpretation, so we are grateful for the reviewer’s suggestions.

2) Related to the above issue, it would be useful to analyze the difference between conditions using different metrics to fully understand what really are different between conditions. The scatter plots shown in various figures do not show drastic differences between awake and anesthetized conditions, as might be indicated by the percent of sublinear responses. It would be useful to characterize the magnitude of sublinear/supralinear effects. For example, one can calculate a fractional change in the mean response. Does this measure show consistent difference between awake and anesthetized conditions?

Thank you for suggesting this analysis. As described above, we now use the fractional deviation to quantify how mixture summations differ from linear sums, which turned out to be a very useful way to express the property of summation (N.B.: noise is amplified for small responses when fractional deviation is used, which is another reason we use the median now). We thank the reviewer for suggesting this analysis.

Reviewer #2 (Public Review):

This study addresses how complex stimuli are represented in neural responses. This is particularly relevant to olfaction because the vast majority of stimuli are complex mixtures that perceptually, are not easy to decompose into parts. Nonetheless, the ability to discern a relevant odor from background odors is essential. This process is easier when neural responses to mixtures reflect the linear sum of the responses to the individual components. The main conclusion of this study is that the linearity of olfactory bulb responses to two-component mixtures increases awake versus anesthetized states. The authors provide some evidence to support this claim. However, this could be better quantified and there is a temporal aspect of linearization that is not addressed. Perhaps the most interesting aspect of the study is the difference in linearity between the dendrites and the somata of the mitral/tufted cells. But a statistical analysis of this finding was not evident. Overall a mechanistic or functional approach to understanding these findings is lacking. The differences linearity between the anesthetized and awake are simply explained by response saturation anesthetized animals. There are hints at mechanism by which linearity is supported in the OB with comparisons between soma and dendrite but these are not well developed. There is a model that addresses the functional significance of linearity but this is only supplemental and not well described.

Thank you for appreciating the significance of our work, and for your constructive comments.

Reviewer #3 (Public Review):

Adefuin et al use multiphoton imaging of M/T cell responses to investigate whether neuronal representations of binary mixtures can be explained as a sum of the components. The current view in the field (built largely from studies in anesthetized animals), is that mixture summation is non-linear and increases with the degree in glomerular response overlap elicited by the components. The authors reproduce these results and ask whether the same phenomenon is observed in the awake state, in particular when the animals are engaged in an odor discrimination task. Unlike in the anesthetized state, the authors find that mixture representations are linear in the awake brain. They use a series of systematic behavioral paradigms to show that the observed linearity in the awake state (compared to anesthetized) is not dependent on task engagement (reward is given randomly, post-odor) or stimulus relevance (reward is given before odor). While the experiments are well done and the data is presented clearly, I have several major concerns about the interpretation of their results.

1) Given the data the authors present, it is unclear if one can conclude that the olfactory system is more or less linear in the awake state compared to the anaesthetised one. What seems to change most across the awake vs. anesthetized state is the response amplitude. Responses appear to be ~3x smaller in the awake mice. In the anesthetized state, non-linearity seems most apparent for large response amplitudes (>5 dF/F) with mixture responses being sub-linear, most likely due to saturation effects. The authors themselves do an analysis in Figure 6 - supplement 1 to show that most of the observed non-linearity in the anesthetized animals can be explained away after accounting for amplitude normalisation. The authors use this analysis to comment that the level of linearity is the same across all the three awake states, but the same figure shows that it is in fact the same even for the anaesthetized state.

To put it differently, it is indeed true from the authors data that the OB response gain is significantly lower in the awake state, but it is unclear if the summation is more linear if measured at similar response amplitude regimes in both awake and anaesthetised mice.

Thank you for the valuable comments. We agree that many differences between the anaesthetised vs. awake states should have been taken into account when comparing the linearity of summation. We address the reviewer’s concern now by expressing the deviation as a fraction of the predicted, linear sum of component responses. Further, we also considered another factor that could influence the anaesthetised vs. awake comparison, namely, the trial-by-trial variability. This is reproduced below.

Figure R1: comparison of mixture summation for the early phase of responses, expressed as the fractional deviation.

2) The authors argue that keeping response amplitudes small in the awake brain prevents sub-linear summation and therefore may lead to better mixture decomposition. They do a decoding analysis in anaesthetised mice to show that linear mixture representations (instead of using observed sub-linear representations) make odor classification easier. However, I find this analysis uninformative and misleading. It is no surprise that the decoders trained on single odor representations should perform better (or equivalent) when using linear sums as input instead of observed sub-linear representations. The authors use this observation to suggest that this mechanism aids discrimination ability in the awake state. However, given that even the single odor responses are much weaker and noisier in the awake state, it is likely that even the single odor discrimination ability is poorer in the awake state. By the same logic, mixture decomposition might be also much poorer in the awake brain than the anesthetized brain, even though summation is more linear, just because responses are weaker and noisier. In my opinion, the authors should compare decoding accuracy across awake vs. anesthetized responses if they want to assert that linearisation of responses in the awake brain leads to easier decomposition. Because otherwise, while linearisation in principle can aid decomposition, at least in the form that the authors observe here, it may come at a high cost on signal-to-noise ratio which would undo the gain that linearity provides, in principle, for discrimination.

Thank you very much for the insight and for the excellent suggestion to consider the discriminability of stimuli. In particular, we now include an analysis where a decoder trained on single responses is tested on observed mixture responses. Surprisingly, despite the substantial differences in the amplitudes of response and trial-by-trial variability, decoders using data from awake mice performed well, even better than anaesthetised data for the late phase of responses. This is now described in the revised figures (revised Fig. 5). We thank the reviewer for the excellent suggestion.

Interestingly, though, the time course of the decoder performance does not correlate well with the linearity of summation. This observation is now described in the abstract (lines 19-21): “…decoding analyses indicated that the data from behaving mice was able to encode mixture responses well, though the time course of decoding accuracy did not correlate with the linearity of summation“.

3) At a more philosophical level, to this Reviewer, it is unclear if anesthesia vs. awake state difference in response should constitute the main focus of the manuscript. The authors explore summation properties under four different brain states, one of which is anaesthesia (also least behaviorally relevant). In three out of four states, they observe that summation is linear. In the fourth (anaesthesia), they observe that summation is sub-linear, but this happens at much larger response amplitude regimes compared to the three awake states sampled, presumably due to saturation. To me, it seems that the Authors here show that mixture summation in the OB, is largely independent of brain state since it is unaffected by whether the animal is task engaged or motivated etc.

Thank you for this thoughtful comment. This has made us reflect on the essence of our study. We believe we make three main observations. First, the anaesthesia vs. awake difference in the property of summation differ, and should be reported, because of the large volume of prior works reporting sublinear summations. However, as the reviewer recommends and as mentioned next, this is no longer the sole focus of our study. Our second observation is that the linearity of summation does not necessarily correlate with the ability to analyse mixtures, based on the decoder performance. We believe it is important to share this observation, since a number of previous studies speculated that nonlinear summation contributes to perceptual difficulty (Bell et al., 1987; Laing, 1994). Third, the decoder performance - especially one that is trained on single odour responses and tested on mixtures - shows differences depending on the awake states, where data from disengaged mice performed particularly poorly. This result is shown in the revised Figure 6. Further, we have edited the abstract and results to ensure that these are clearly communicated. We hope that this is more balanced and reflects the data better.

4) It is unclear how to interpret the dendritic imaging comparison. First, the dendritic signal is pooled across many cells. If any of the cells that are being pooled shows sub-linearity, the pooled population response will look sub-linear, albeit less so than at the single cell level. Second, again like for the anesthetized vs. awake comparison, there is a discrepancy in response amplitudes - dendritic responses are ~2x stronger than the somatic responses and sub-linear summation would be more apparent as one approaches the saturation regime. Third, dendritic responses pool both mitral and tufted, while the somatic data the authors present is predominantly from tufted cells.

Thank you for commenting on ways to further understand the dendritic signal. Indeed, the early prevalence of sublinearity in the apical dendrites does seem to relate to the time course of responses. This is treated more directly in the revised Fig.4 – supplement 1.

To address the averaging effect, we tested how pulled signals may look like in terms of linearity of summation. To roughly approximate pooled responses, we reasoned that neighbouring TC/MC somata have higher chances of belonging to the same glomerulus. Thus, we averaged signals from somatic ROIs (TCs and MCs) from each field of view and calculated the fractional deviation from the linear sum (Fig. R2). While a simplistic averaging of neighbouring somata may not be perfectly accurate, but this analysis indicates that the difference between the apical dendrites vs. somata may not be simply explained by the averaging effect.

Figure R2: Analysis of pooled somatic signals

To approximate how dendritic signals might look like if they were simple averages of somatic responses, we pooled together signals from all TC/MC somata from each field of view, and treated it as “an approximate glomerular signal”. The plot above shows the fractional deviation from the linear sum. MC somata data comes from an additional set of experiments conducted for this rebuttal).

In terms of the unmatched amplitude distributions and trial-by-trial variability across conditions, as the reviewer points out, the issue is similar to the comparison of anaesthetised vs. awake data. To address this, all comparisons are now presented in terms of the median fractional deviations. Further, to explain if mitral cells contributed to the discrepancy in the linearity between the dendritic signal vs. somatic signal, we now provide additional data from 137 MCs (5 fields of view, 3 trained mice performing the mixture task). These changes are described in the revised manuscript (Figure 4- supplement 1).

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:

Reviewer #1:

In this paper, authors did a fine job of combining phylogenetics and molecular methods to demonstrate the parallel evolution across vRNA segments in two seasonal influenza A virus subtypes. They first estimated phylogenetic relationships between vRNA segments using Robinson-Foulds distance and identified the possibility of parallel evolution of RNA-RNA interactions driving the genomic assembly. This is indeed an interesting mechanism in addition to the traditional role for proteins for the same. Subsequently, they used molecular biology to validate such RNA-RNA driven interaction by demonstrating co-localization of vRNA segments in infected cells. They also showed that the parallel evolution between vRNA segments might vary across subtypes and virus lineages isolated from distinct host origins. Overall, I find this to be excellent work with major implications for genome evolution of infectious viruses; emergence of new strains with altered genome combination.

Comments:

I am wondering if leaving out sequences (not resolving well) in the phylogenic analysis interferes with the true picture of the proposed associations. What if they reflect the evolutionary intermediates, with important implications for the pathogen evolution which is lost in the analyses?

We fully appreciate this concern and have explored this extensively. One principle assumption underlying the approach we outline in this manuscript is that the trees analyzed are robust and well- resolved. We use tree similarity as a correlate for relationships between genomic segments, so the trees must be robust enough to support our claims, as we have clarified in lines 128-131. We initially set out to examine a broader range of viral isolates in each set of trees, but larger trees containing more isolates consistently failed to be supported by bootstrapping. Bootstrapping is by far the most widely used methodology for demonstrating support for tree nodes. We provided the closest possible example to the trees presented in this manuscript for comparison. We took all 84 H3N2 strains from 2005-2014 analyzed in replicate trees 1-7 and collapsed these sequences into one tree for each vRNA segment. Figure X-A, specifically provided for the reviewers, illustrates the resultant collapsed PB2 tree, with bootstrap values of 70 or higher shown in red and individual strains coded by cluster and replicate. As expected, the majority of internal nodes on such a tree are largely unsupported by bootstrapping, indicating that relaxing our constraint of 97% sequence identity increases the uncertainty in our trees.

Because we agree with Reviewers #1 and #3 on the critical importance of validating our approach, we determined the distances between these new collapsed trees using a complementary approach, Clustering Information Distances (CID), that is independent of tree size (Supplemental Figure 4B and Figure X-B & X-C). Larger trees containing all sequences yielded pairwise vRNA relationships that are largely similar to those we report in the manuscript (R2 = 0.6408; P = 3.1E-07; Figure X-B vs. X-C), including higher tree similarity between PB2 and NA over NS. This observation strengthens the rationale to focus on these segments for molecular validation and correlate parallel evolution to intracellular localization in our manuscript (Figure 7). However, tree distances are generally higher in Figure X-C than in Figure X-B, which we might expect if poorly supported nodes in larger trees artificially inflate phylogenetic signal. Given the overall similarity between Figures X-B and X-C, both methods yield largely comparable results. We ultimately relied upon the more robust replicate trees with stronger bootstrap support.

Lines 50-51: Can you please elaborate? I think this might be useful for the reader to better understand the context. Also, a brief description on functional association between different known fragments might instigate curiosity among the readers from the very beginning. At present, it largely caters to people already familiar with the biology of influenza virus.

We have added additional information to reflect the complexity of intersegmental interactions and the current standing of the field (lines 49-52).

Lines 95-96 Were these strains all swine-origin? More details on these lineages will be useful for the readers.

We have clarified that all strains analyzed were isolated from humans, but were of different lineages (lines 115-120).

Lines 128-132: I think it will be nice to talk about these hypotheses well in advance, may be in the Introduction, with more functional details of viral segments.

We incorporated our hypotheses regarding tree similarity into the existing discussion of epistasis in the Introduction (lines 74-75 and 89-106).

Lines 134-136: Please rephrase this sentence to make it more direct and explain the why. E.g. "... parallel evolution between PB1 and HA is likely to be weaker than that of PB1 and PA".

The text has been modified (lines 165-168).

Lines 222-223: Please include a set of hypotheses to explain you results? Please add a perspective in the discussion on how this contribute might to the pandemic potential of H1N!?.

We have added in our interpretation of the results (lines 259-264) and expanded upon this in the Discussion (lines 418-422).

Lines 287-288: I am wondering how likely is this to be true for H1N1.

We have expanded on this in the Discussion (lines 409-410).

Reviewer #2:

The influenza A genome is made up of eight viral RNAs. Despite being segmented, many of these RNAs are known to evolve in parallel, presumably due to similar selection pressures, and influence each other's evolution. The viral protein-protein interactions have been found to be the mechanism driving the genomic evolution. Employing a range of phylogenetic and molecular methods, Jones et al. investigated the evolution of the seasonal Influenza A virus genomic segments. They found the evolutionary relationships between different RNAs varied between two subtypes, namely H1N1 and H3N2. The evolutionary relationships in case of H1N1 were also temporally more diverse than H3N2. They also reported molecular evidence that indicated the presence of RNA-RNA interaction driving the genomic coevolution, in addition to the protein interactions. These results do not only provide additional support for presence of parallel evolution and genetic interactions in Influenza A genome and but also advances the current knowledge of the field by providing novel evidence in support of RNA-RNA interactions as a driver of the genomic evolution. This work is an excellent example of hypothesis-driven scientific investigation.

The communication of the science could be improved, particularly for viral evolutionary biologists who study emergent evolutionary patterns but do not specialise in the underlying molecular mechanisms. The improvement can be easily achieved by explaining jargon (e.g., deconvolution) and methodological logics that are not immediately clear to a non-specialist.

We have clarified or eliminated jargon wherever possible throughout the text.

The introduction section could be better structured. The crux of this study is the parallel molecular evolution in influenza genome segments and interactions (epistasis). The authors spent the majority of the introduction section leading to those two topics and then treated them summarily. This structure, in my opinion, is diluting the story. Instead, introducing the two topics in detail at the beginning (right after introducing the system) then discussing their links to reassortments, viral emergence etc. could be a more informative, easily understandable and focused structure. The authors also failed to clearly state all the hypotheses and predictions (e.g., regarding intracellular colocalisation) near the end of the introduction.

We restructured the Introduction with more background on genomic assembly in influenza viruses, as requested by two reviewers (lines 43-52), more discussion of epistasis (lines 58-63) and provided a more thorough discussion of all hypotheses (lines 74-77, 88-92, 94-95, 97-106).

The authors used Robinson-Foulds (RF) metric to quantify topological distance between phylogenetic trees-a key variable of the study. But they did not justify using the metric despite its well-known drawbacks including lack of biological rational and lack of robustness, and particularly when more robust measures, such as generalised RF, are available.

We agree that RF has drawbacks. To address this, we performed a companion analysis using the Clustering Information Distance (CID) recently described by Smith, 2020. The mean CID can be found in Figure S4, the standard error of the mean in Figure S5, and networks depicting overall relationships between segments by CID in Figure S7E-S7H. To better assess how well RF and CID correlate with each other across influenza virus subtypes and lineages, we reanalyzed all data from both sets of distance measures by linear regression (Figure 3B, 4B-C, 5B, S6 and S9). Our results from both methods are highly comparable, which we believe strengthens our conclusions. Both analyses are included in the resubmission (lines 86-89; 162; 164; 187-188; 199-200; 207-208; 231-234; 242-244; 466-470).

Figure 1 of the paper is extremely helpful to understand the large number of methods and links between them. But it could be more useful if the authors could clearly state the goal of each step and also included the molecular methods in it. That would have connected all the hypotheses in the introduction to all the results neatly. I found a good example of such a schematic in a paper that the authors have cited (Fig. 1 of Escalera-Zamudio et al. 2020, Nature communications). Also this methodological scheme needs to be cited in the methods section.

We provided the molecular methods in a schematic in Figure 1D and the figure is cited in the Methods (lines 310; 440; 442; 456; 501).

Finally, I found the methods section to be difficult to navigate, not because it lacked any detail. The authors have been excellent in providing a considerable amount of methodological details. The difficulty arose due to the lack of a chronological structure. Ideally, the methods should be grouped under research aims (for example, Data mining and subsampling, analysis of phylogenetic concordance between genomic segments, identifying RNA-RNA interactions etc.), which will clearly link methods to specific results in one hand and the hypotheses, in the other. This structure would make the article more accessible, for a general audience in particular. The results section appeared to achieve this goal and thus often repeat or explain methodological detail, which ideally should have been restricted to the methods section.

We organized the Methods section by research aims as suggested. However, some discussion of the methods were retained in the Results section to ensure that the manuscript is accessible to audiences without formal training in phylogenetics.

Reviewer #3:

The authors sought to show how the segments of influenza viruses co-evolve in different lineages. They use phylogenetic analysis of a subset of the complete genomes of H3N2 or the two H1N1 lineages (pre and post 2009), and use a method - Robinson-Foulds distance analysis - to determine the relationships between the evolutionary patterns of each segment, and find some that are non-random.

1) The phylogenetic analysis used leaves out sequences that do not resolve well in the phylogenic analysis, with the goal of achieving higher bootstrap values. It is difficult to understand how that gives the most accurate picture of the associations - those sequences represent real evolutionary intermediates, and their inclusion should not alter the relationships between the more distantly related sequences. It seems that this creates an incomplete picture that artificially emphasizes differences among the clades for each segment analyzed?

Reviewer #1 raised the same concern. Please refer to our response at the beginning of this letter where we address this issue in depth.

2) It is not clear what the significance is of finding that sequences that share branching patterns in the phylogeny, and how that informs our understanding of the likelihood of genetic segments having some functional connection. What mechanism is being suggested - is this a proxy for the gene segments having been present in the same viruses - thereby revealing the favored gene segment combinations? Is there some association suggested between the RNA sequences of the different segments? The frequently evoked HA:NA associations may not be a directly relevant model as those are thought to relate to the balance of sialic acid binding and cleavage associated with mutations focused around the receptor binding site and active site, length of NA stalk, and the HA stalk - does that show up in the overall phylogeny of the HA and NA segments? Is there co-evolution of the polymerase gene segments, or has that been revealed in previous studies, as is suggested?

We clarified our working hypotheses in the Introduction (lines 89-106) and what is known about the polymerase subunits (lines 92-93). Our data do suggest that polymerase subunits share similar evolutionary trajectories that are more driven by protein than RNA (lines 291-293; Figure 2A and 6). The point about epistasis between HA and NA arising from indirect interactions is entirely fair, but these studies are nonetheless the basis for our own work. We have clarified the distinction between these prior studies and our own in the text (lines 60-63 and 74-75). Moreover, our protein trees built from HA and NA recapitulate what has been shown previously, which we highlight in the text (lines 293-296; Figure 6 and Figure S10). We also clarified our interpretation of tree similarity throughout the text (lines 165-168; 190-191; 261-264; 323-326; 419-423).

The mechanisms underlying the genomic segment associations described here are not clear. By definition they would be related to the evolution of the entire RNA segment sequence, since that is being analyzed - (1) is this because of a shared function (seems unlikely but perhaps pointing to a new activity), or is it (2) because of some RNA sequence-associated function (inter-segment hybridization, common association of RNA with some cellular or viral protein)? (3) Related to specific functions in RNA packaging - please tell us whether the current RNA packaging models inform about a possible process. Is there a known packaging assembly process based on RNA sequences, where the association leads to co-transport and packaging - in that case the co-evolution should be more strongly seen in the region involved in that function and not elsewhere? The apparent increased association in the cytoplasm of the subset of genes examined for the single virus looks mainly in the cytoplasm close to the nucleus - suggesting function (2) and/or (3)?.

It is difficult to figure out how the data found correlates with the known data on reassortment efficiency or mechanisms of systems for RNA segment selection for packaging or transport - if that is not obvious, maybe you can suggest processes that might be involved.

We provided more context on genomic packaging in the Introduction, including the current model in which direct RNA interactions are thought to drive genomic assembly (lines 43-53). Although genomic segments are bound by viral nucleoprotein (NP), accurate genomic assembly is theorized to be a result of intersegment hybridization rather than driven by viral or cellular protein. We further clarified our hypotheses regarding the colocalization data in the Results section to make the proposed mechanism clearer (lines 313-326).

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.

Author Response

Reviewer #1 (Public Review):

Bornstein and colleagues address an important question regarding the molecular makeup of the different cellular compartments contributing to the muscle spindle. While work focusing on single components of the spindle in isolation - proprioceptors, gamma-motor neurons, and intrafusal muscle fibres - have been recently published, a comprehensive analysis of the transcriptome and proteome of the spindle was missing and it fills an important gap considering how local translation and protein synthesis can affect the development and function of such a specialised organ.

The authors combine bulk transcriptome and proteome analysis and identify new markers for neuronal, intrafusal, and capsule compartments that are validated in vivo and are shown to be useful for studying aspects of spindle differentiation during development. The methodology is sound and the conclusions in line with the results.

We thank the reviewer for highlighting the importance of our study.

I feel a bit more analysis regarding the specificity and developmental expression profiles of the identified markers would be a great addition. In particular:

• Are any of the proprioceptive sensory neurons markers specific for fibres innervating the muscle spindles or also found in Golgi tendon organs?

We thank the reviewer for the important question, following which we performed two additional analyses. First, in order to study the specificity of spindle afferent genes we identified, we examined the overlap between our list of 260 potential proprioceptive neuron genes and markers for the three proprioceptive neurons subtypes (Ia, II and Ib) identified by Wu and colleagues (Wu et al. 2021). As shown in the newly added Figure 1- figure supplement 2F, while we found many genes that are common to all subtypes, 69 genes exclusively overlapped with subtype markers (22 genes with type Ia neurons, 45 genes with type II neurons and 2 genes with both; lists are shown in Supplementary File 4). These results suggest that the 69 genes are expressed by muscle spindle afferents and not by GTO afferents.

Second, to study the specificity of our validated markers, we examined the expression of ATP1a3, VCAN and GLTU1, marking proprioception neurons, extracellular matrix and outer capsule, respectively, in GTOs. Results showed that all three markers were also detected in the different tissues composing the GTOs (newly added Figure 3 – figure supplement 3, below). As ATP1a3 is not in the 69 unique marker list, this analysis verified that it is expressed by all proprioceptive neurons. The expression of both VCAN and GLUT1 in GTO capsules highlights the similarity between the capsules of the two proprioceptors.

• On the same line are any of the gamma motor neurons markers found also in alpha?

We thank the reviewer for raising this issue. Following the reviewer’s question, we conducted a detailed analysis of the expression of potential γ motor neuron genes. To this end, we first generated a list of α-motor neurons genes in our data by performing ranked GSEA using published expression profiles of these neurons (Blum et al., 2021). Then, we compared between the three lists of neuronal genes, i.e. γ motor neurons, α motor neurons and proprioceptive neurons (newly added Figure 1 – figure supplement 2G), and found an overlap between the three lists. Nonetheless, we also identified 40 spindle genes that are specific to γ motor neuron (Figure 1 – figure supplement 2G and Supplementary File 4) and, therefore, are potential markers for these neurons.

• How early expression of ATP1A3 is found in neurons at the spindle or fibres starting to innervating the muscle? A couple of late embryonic timepoints would be great.

We thank the reviewer for this suggestion. We performed late embryonic (E15.5-E17.5) staining for ATP1a3, which showed its expression as early as E15.5 (new Figure 4 – figure supplement 1).

• Given that the approach used allows to obtain insights on whether local translation plays a major role into the differentiation of the spindle it would be interesting to assess whether the proprioceptor and gamma motor neuron markers identified are also found in the cell body or exclusively at the spindle.

The reviewer raises an interesting question about local translation of the neuronal genes. Going through the literature, several lines of evidence indicate that the genes expressed at the neuronal end are also expressed in the neuron soma. In a study on retinal ganglion cell translatome, Holt and colleagues found that the axonal translatome is a subset of the significantly larger somal translatome (Shigeoka et al., Cell, 2016). Similarly, a study by Shuman and colleagues that compared the translatome of neuronal cell bodies, dendrites, and axons of rat hippocampal neurons showed that many common genes are translated, albeit at different levels (Glock et al., PNAS, 2021). Finally, following the reviewer’s suggestion, we studied the expression of ATP1a3 in the DRG, and found it to be expressed there as well (Figure L1). Thus, we predict that the markers we found in the neurons ends are likely also expressed in the soma. While this issue is very interesting, we believe that further validation of our assumption exceeds the scope of this study.

Figure L1. ATP1a3 expression in the DRG. Confocal images of DRG sections from adult PValb-Cre;tdTomato mice stained for ATP1a3 (magenta). Scale bars represent 50 μm.

Altogether, this is a novel and important work that will benefit scientists studying the neuromuscular and musculoskeletal systems by pushing the field toward an holistic understanding of the muscle spindle. These datasets in combination with the previous ones can be used to develop new genetic and viral strategies to study muscle spindle development and function in healthy and pathological states by analysing the roles and relative contributions of different components of this fascinating and still mysterious organ.

We thank again the reviewer for highlighting the importance of our study.

Reviewer #2 (Public Review):

The data presented are of high quality. Through complementary experiments involving the isolation of masseter muscle spindles, the authors perform RNA-seq and proteomic analysis, and identify genes and proteins that are differentially expressed in the muscle spindle versus the adjacent muscle fiber, and proteins that accumulate specifically in capsule cells and nerve endings. These data, while essentially descriptive, provide important information about the developmental framework of the sensory apparatus present in each muscle that accounts for its tension/contraction state. The data presented thus allow for a better characterization of muscle spindles and provide the community with a set of new markers for better identification of these structures. Analysis of the expression pattern of the Tomato reporter in transgenic animals under the control of Piezo2-CRE, Gli1-CRE and Thy1-YFP reporter reinforces the findings and the specificity of the expression pattern of the specific genes and proteins identified by the multi-omics approach and further validated by immunohistochemistry.

We thank the reviewer for the positive and encouraging feedback.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Marmor and colleagues reanalyze a previously published dataset of chronic widefield Ca2+ imaging from the dorsal cortex of mice as they learn a go/no-go somatosensory discrimination task. Comparing hit trials that have a distinct history (i.e. are preceded by distinct trial types), the authors find that hit trials preceded by correct rejections of the nontarget stimulus are associated with larger subsequent neural responses than trials precede by other hits, across the cortex. The authors analyze the time course over which this effect emerges in the barrel cortex (BC) and the rostrolateral visual area (RL), and find that its magnitude increases as the animals become expert task performers. Although the findings are potentially interesting, I, unfortunately, believe that there are important methodological concerns that could put them into question. I also disagree with the rationale that singles out BC and RL as being especially important for the emergence of trial history effects on neural responses during decision-making. I detail these points below .

1) The authors did not perform correction for hemodynamic contamination of GCaMP fluorescence. In widefield imaging, blood vessels divisively decrease neural signals because they absorb green-wavelength photons, which could lead to crucial confounds in the interpretation of the main results because of neurovascular coupling, which lags neural activity by seconds. For example, if a reward response from the previous trial is associated with a lagged hemodynamic contamination that artificially decreases the signal in the following trial, one could get artificially higher activity in trials that were not preceded by a reward (i.e. CR), which is what the authors observed. Ideally, the experiments would be repeated with proper hemodynamic correction, but at the very least the authors should try to address this with control analyses.

Done. We basically redone the experiment with proper hemodynamic correction and maintained trial history results. Please see point 1 above for more details (Figures S4 and S5). In addition to hemodynamic controls, we also present novel two-photon single cell data with similar results in Figure S6. We also added a dedicated section for this in the Methods section (pg. 12).

For example, what is the time course of reward-related responses in BC and elsewhere?

In general, and specifically in BC, reward related responses return to baseline up to 5 seconds after the start of the reward period and at least 5 seconds before the stimulus presentation of the next trial. In the novel experiments we even extended the baseline period by an additional 2 seconds just in case. Trial history information was still present with an extended inter-trial interval.

The text now reads (pg. 4): "We further report that responses during the reward period in cortex and specifically in BC went back to baseline 4-5 seconds after the start of the reward period and 6-8 seconds before the presentation of the next stimulus (total inter-trial interval ranged between 10-12 seconds)."

Do hemodynamics artifacts have a trial-by-trial correlation with the subsequent trial history effect?

We have now done the proper hemodynamic control (Figure 2) and we did not find a strong effect of hemodynamic responses on trial history information.

What is the learning time course of reward responses?

Responses during the reward period as a function of learning were not significantly modulated. We further show the whole learning profile for BC response during the reward period in Author response image 1.

Author response image 1.

Response in BC averaged during the reward period (2-4 sec after texture stop) as a function of learning for each mouse separately.

The text now reads (pg. 4): "In addition, responses in BC during the reward period were not consistently modulated as a function of learning (p>0.05; Wilcoxon signed-rank test between naïve and expert, BC response averaged during the reward period, 2-4 seconds after stimulus onset; n=7 mice). Taken together, we find that direct responses from the reward period do not effect history-related responses during the next trial."

Note that I don't believe the FA-Hit condition analysis that the authors have already presented provides adequate control, as punishment responses are also pervasive in the cortex and therefore suffer from the same interpretational caveat. Unfortunately, I believe this is a serious methodological issue given the above. However, I will proceed to take the reported results at face value .

We hope that our additional control analysis regarding the hemodynamic controls are satisfactory.

2) The statistics used to assess the effect of trial history over learning are inadequate (e.g., Fig 2b). The existence of a significant effect in one condition (e.g., CR-Hit vs. Hit-Hit in expert) but not in another (e.g., same comparison in naive) does not imply that these two conditions are different. This needs to be tested directly. Moreover, the present analysis does not account for the fact that measures across learning stages are taken from the same animals. Thus, the appropriate analysis for these cases would be to first use a two-way ANOVA with repeated measures with factors of trial history and learning stage (or equivalent non-parametric test) and then derive conclusions based on post hoc pairwise tests, corrected for multiple comparisons .

Done. We performed 2 way ANOVA as suggested and found significant history and learning effects along with a significant interaction effect for BC.

The text now reads (pg. 4): "This difference was significant during the stim period in learning and expert phases across mice (Fig. 2b; 2-way ANOVA with repeated measures; DF (1-6) F=51 p<0.001, DF (2-12) F=18 p<0.001, DF(2-12) F=5 p<0.05 for trial history, learning and the interaction between trial history and learning; Post hoc Tukey analysis p<0.05 for trial history in learning and expert phases; p>0.05 in the naïve phase)."

3) I am not convinced that BC and RL are especially important for trial-history-dependent effects. Figures 4 and 5 suggest that this modulation is present across the cortex, and in fact, the difference between CR-Hit and Hit-Hit in some learning stages appears stronger in other areas. BC and RL do have the highest absolute activity during the epochs in Figs 4 and 5, but I would argue that this is likely due to other aspects of the task (e.g., touch) and therefore is not necessarily relevant to the issue of trial history .

Done. First, we would like to point out that RL during the pre period displays the largest difference between the CR-Hit and Hit-Hit conditions (Fig. 5c bottom). Second, we now show difference maps (i.e., activity in CR-Hit minus Hit-Hit) which clearly show a positive activity patch in BC during the stim period for 5 out of the 7 mice (Fig. S10a). Example maps also highlight RL during the pre period (Fig. S10b). We note that activity patches somewhat spread over to other areas and also slightly vary across mice. This is why the grand average may slightly average out trial history information. Taken together, we strongly feel that during the pre period, trial history information emerges in RL (and adjacent posterior association areas) which shift towards BC during the stim period

Nevertheless, we agree with the reviewer that other areas (that do not necessarily display high activity) may encode trial history information and we now clearly report this in the text (pg. 5): "We note that other areas, e.g., different association areas, also encoded historydependent information especially during learning and expert phases. In addition, we present activity difference maps between CR-Hit and Hit-Hit conditions during the stim period (Fig. S10a). These maps clearly show the highest trial history information (i.e., difference in activity) in BC. Taken together, these results indicate that BC encodes history-dependent information that emerges during the stim period and just after learning. "

And also in (pg. 6): " In addition, we present activity difference maps between CR-Hit and HitHit conditions during the pre period (Fig. S10b). These maps localize trial history information to RL which also spreads to other adjacent association areas. Moreover, activity patches slightly vary across the different mice which may affect the grand average (averaged across mice) of each area."

4) Because of similar arguments to the above, and because this was not directly assessed, I do not believe the conclusion that history information emerges in RL and is transferred to BC is warranted. For instance, there is no direct comparison between areas, but inspection of the ROC plots in Fig 6b suggests that history information emerges concomitantly across cortical areas. I suggest directly comparing the time course between these and other areas

Done. We now add example history AUC maps and quantify history AUC for all 25 areas during the pre and stim periods. During the pre period (Fig. 6), AUC values are concentrated around the RL (and other PPC areas), whereas during the stim periods AUC values shift to BC. Again, due to the inter-mouse variability, these differences are slightly averaged out which also makes it tough to have strong statistical test (with only 7 mice).

The text now reads (pg. 7): "We next calculated the history AUC for each pixel during either the pre or stim period. The history AUC maps during the pre period display AUC values around the RL areas (Fig. 6f). In contrast, the history AUC maps during the stim period display AUC values mostly in BC (Fig. 6g). Quantified across 25 areas and averaged across mice, RL displays the highest history AUC during the pre period, whereas BC displays the highest history AUC values during the stim period (Fig. 6h). We note that other cortical areas such as other association areas also display high history AUC values. Taken together, we find that trial history emerges in RL before the texture arrives and then shifts to BC during stimulus presentation. "

5) How much is task performance itself modulated by trial history? How does this change over the course of learning? These behavioral analyses would greatly help interpret the neural findings and how this trial history might be used behaviorally .

Done, we have now calculated the dprime for Hit-Hit and CR-Hit trials separately. We find no significant differences between conditions both within and across mice (see Fig. S2 below).

The text now reads pg. 3): "We note that learning curves that are calculated separately for each pair (i.e., either a preceding Hit or CR trial) were not significantly different (Fig. S2)."

Reviewer #2 (Public Review):

Marmor et al. mine a previously published dataset to examine whether recent reward/stimulus history influences responses in sensory (and other) cortices. Bulk L2/3 calcium activity is imaged across all of the dorsal cortex in transgenic mice trained to discriminate between two textures in a go/no-go behavior. The authors primarily focus on comparing responses to a specific stimulus given that the preceding trial was or was not rewarded. There are clear differences in activity during stimulus presentation in the barrel cortex along with other areas, as well as differences even before the second stimulus is presented. These differences only emerge after task learning. The data are of high quality and the paper is clear and easy to follow. My only major criticism is that I am not completely convinced that the observed difference in response is not due to differences in movement by the animal on the two trial types. That said, the demonstration of differences in sensory cortices is relatively novel, as most of the existing literature on trial history effect demonstrates such differences only in higher-order areas .

Major :

1a) The claim that body movements do not account for the results is in my view the greatest weakness of the paper - if the difference in response simply reflects a difference in movement, perhaps due to "excitement" in anticipation of reward after not receiving one on CR-H vs. HH trials, then this should show up in movement analysis. The authors do a little bit of this, but to me, more is needed .  

Done. We have now extensively and carefully analyzed body and whisker movements for CRHit and Hit-Hit conditions. First, In the figure below we decomposed body movements into 22 different body parts using DeepLabCut. In short, we find no significant difference between CRHit and Hit-Hit conditions in each body part separately (Fig. S7 below). This was true for the naïve, learning and expert phases. Please see additional analyses in the points below.

This is now reported in the text (pg. 4): “In addition, we performed a more detailed body and whisker analysis, e.g., decomposing the movement to different body parts and obtaining single whisker dynamics. These analyses did not find significant differences in movement parameters between CR-Hit and Hit-Hit conditions (Fig. s7 and s8).”

First, given the small sample size and use of non-parametric tests, you will only get p<.05 if at least 6 of the 7 mice perform in the same way. So getting p>.05 is not surprising even if there is an underlying effect. This makes it especially important to do analyses that are likely to reveal any differences; using whisker angle and overall body movement, which is poorly explained, is in my opinion insufficient. An alternative approach would be to compare movements within animals; small as the dataset is, it is feasible to do an animal-by-animal analysis, and then one could leverage the large trial count to get much greater statistical power, foregoing summary analyses that pool over only n=7 .

We agree with this point and are have now dramatically improved our statistical analysis.

1) We now perform within mouse statistics for responses in BC during naïve, learning and expert (see Fig. S4 below). In short, we find statistical significance for 7 out of 7 mice during the expert phase, 6 out of 7 mice in the learning phase and 0 out of 7 in the naive phase. For RL during the pre period we find significant difference in 5 out of 7 expert mice.

This is now reported in the text (pg. 4): "In addition, a statistical comparison between CR-Hit and Hit-Hit responses within each mouse separately maintained significance for expert (7/7 mice Mann-Whitney U-test p<0.05) and learning (6/7 mice) but not for naïve (0/7 mice. Fig. S3)."

And also in (pg. 5): "In addition, a statistical comparison between CR-Hit and Hit-Hit responses in RL within each mouse separately maintained significance for expert (5/7 mice; MannWhitney U-test p<0.05)."

2) We would like to point out that we have now added 3 additional mice (with hemodynamics control) and performed within mouse statistics in BC and RL (Fig. S5), adding to our initial observations.

3) In terms of body movements, we now performed within mice statistics and compared body movements between CR-Hit and Hit-Hit conditions. In general, most mice did not show a significant difference in body movements or whisker envelope.

This is now reported in the text (pg. 4): "A within mouse statistical comparison between body or whisker parameters in CR-Hit and Hit-Hit maintained a non-significant difference in expert (1/7 mice displayed a significant difference; Mann-Whitney U-test p>0.05), learning (2/7 mice) and naïve (0/7 mice)."

And also in (pg. 4): "Body movements and whisker parameters did not significantly differ between CR-Hit and Hit-Hit conditions during the pre-period (Similar to the stim period. Across and within mice. P>0.05; Mann-Whitney U-test)."

In summary, we have now substantially improved our statistical analysis and further decomposed the body movements, maintaining the trial history results.

The authors only consider a simple parametrization of movement (correlation across successive frames), and given the high variability in movement across animals, it is likely that different mice adopt different movements during the task, perhaps altering movement in specific ways. Aggregating movement across different body parts after an analysis where body parts are treated separately seems like an odd choice - perhaps it is fine, but again, supporting evidence for this is needed. As it stands, it is not clear if real differences were averaged out by combining all body parts, or what averaging actually entails .

Please see the above point where we decomposed body movements (Fig. S7 and Methods section in Pg. 14).

If at all possible, I would recommend examining curvature and not just the whisker angle, since the angle being the same is not too surprising given that the stimulus is in the same place. If the animal is pressing more vigorously on CR-H trials, this should result in larger curvature changes .

Done. We now decompose whisker dynamics (i.e., curvature) using DeepLabCut (Fig. S8 see below). In general, we find no significant differences in whisker parameters between Hit-Hit and CR-Hit conditions.

This is now reported in the text (pg. 4): "In addition, we performed a more detailed body and whisker analysis, e.g., decomposing the movement to different body parts. This analysis did not find significant differences between CR-Hit and Hit-Hit conditions (Fig. S7 and S8)."

Finally, the authors presumably have access to lick data. Are reaction times shorter on CR-H trials? Is lick count or lick frequency shorter?

Done. We now calculated lick reaction time and lick rate and find a significant difference for the lick reaction time but not in lick rate. We show a figure below for the reviewer and report this in the text

The text now reads (pg. 3): "In addition, the lick reaction time (but not the lick rate) between Hit-Hit and CR-Hit were significantly different (p<0.05; Wilcoxon signed-rank test) ,maybe indicating a more considered response after a previous stop signal."

If movement differs across trial types, it is entirely plausible that at least barrel cortex activity differences reflect differences in sensory input due to differences in whisker position/posture/etc. This would mitigate the novelty of the present results .

As detailed above, have now meticulously analyzed the whisker parameter differences between both conditions and did not find any significant differences.

1b) Given the importance of this control to the story, both whisker and body movement tracking frames should be explicitly shown either in the primary paper or as a supplement. Moreover, in the methods, please elaborate on how both whisker and body tracking were performed .

Done. Please see Figs. S7 and S8 for tracking frames. This is now detailed in the above points and also the revised relevant methods section

2) .Did streak length impact the response? For instance, in Fig. 1f "Learning", there is a 6-trial "no-go" streak; if the data are there, it would be useful to plot CR-H responses as a function of preceding unrewarded trials.

Done. We have now calculated response in CR-Hit as a function of the number of preceding CRs. In general, we obtain inconsistent results across mice that may be due to the small number of trials that have more than one preceding CR. Nevertheless, some mice have a trend, sometimes significant, in which CR-Hit responses are higher for longer CR preceding streaks. This is especially true during the learning phase. We have decided not to include this in the manuscript and present this figure only to the reviewer.

Author response:

Reviewer #1 (Public Review):

This is an important and very well conducted study providing novel evidence on the role of zinc homeostasis for the control of infection with the intracellular bacterium S. typhimurium also disentangling the underlying mechanisms and providing clear evidence on the importance of spatio-temporal distribution of (free) zinc within the cell.

We thank the reviewer for the positive comments.

1) It would be important to provide more information on the genotype of mice.

As suggested by the reviewer, we have added the detailed genotype of Slc30a1flagEGFP/+ and Slc30a1fl/flLysMCre mice to the revised supplementary Figure supplement 10.

2) It is rather unlikely that C57Bl6 mice survive up to two weeks after i.p. injection of 1x10E5 bacteria.

According to the reviewer comment, we have tested survival rate using a group of our experimental animals and C57BL/6 wild type.

The Salmonella stain is a gift from our friend, Professor Ge Bao-xue. We have sent this stain for genetic characterisation which we found 100% identity to Salmonella enterica Typhimurium with many strains originated from poultry. One of them is Salmonella enterica subsp. enterica serovar Typhimurium strain MeganVac1 (Accession: CP112994.1), a live attenuated stain. We hope that this would support the relationship between the high infectious dose and mice survive.

Author response image 1.

(A) Survival rate of Slc30a1fl/fl and Slc30a1fl/flLysMCre (n = 14-15/group) and (B) Survival rate of C57BL/6 wild type (n = 8) after Salmonella infection for two weeks. (C) A fulllength sequence (1,478 bases) of 16S rDNA genes sequences of Salmonella stain and (D) the sequencing electropherogram.

3) To be sure that macrophages Slc30A1 fl/fl LysMcre mice really have an impaired clearance of bacteria it would be important to rule out an effect of Slc30A1 deletion of bacterial phagocytosis and containment (f.e. evaluation of bacterial numbers after 30 min of infection).

As the reviewer advised, we have repeated the experiment and measured the bacterial numbers after 30 min of infection (dashed line in A). The results show that there is no statistical difference in the bacterial numbers after 30 min between Slc30a1fl/flLysMCre and Slc30a1fl/fl BMDMs. Therefore, the reduction of bacterial numbers after 24 hours occurs due to the impairment of intracellular pathogen-killing capacity as the reviewer pointed out.

Author respnse image 2.

(A) Time course of the intracellular pathogen-killing capacity of Salmonellainfected Slc30a1fl/flLysMCre and Slc30a1fl/fl BMDMs measured in colony-forming units per ml (n = 5). (B) Fold change in Salmonella survival (CFU/mL) at different time points from A. (C) Representative images of Salmonella colonies on solid agar medium at 24 hours. Data are represented as mean ± SEM. P values were determined using 2-tailed unpaired Student’s t-test. P<0.05, *P<0.01, and ns, not significant.

4) Does the addition of zinc to macrophages negatively affect iNOS transcription as previously observed for the divalent metal iron and is a similar mechanism also employed (CEBPß/NF-IL6 modulation) (Dlaska M et al. J Immunol 1999)?

The reviewer has raised an important point here since free zinc also play a role in multiple levels of cellular signaling components (Kembe et al., 2015). Dlaska and colleague reported that NF-IL6, a protein responsible for iNOS transcription is negatively regulated by iron perturbation under IFNg/LPS stimulation in macrophages (Dlaska and Weiss, 1999). As the reviewer suggested, our results showed that zinc supplementation decreases the iNOS expression in macrophages after Salmonella infection, suggesting that free zinc might play a role in iNOS regulation.

However, in Slc30a1fl/flLysMCre macrophages, despite increase intracellular free zinc, lacking Slc30a1 also induces Mt1, a zinc reservoir which might negatively affect NO production (Schwarz et al., 1995) or alternatively inhibits iNOS through NF-kB pathway (Cong et al., 2016) as reported by previous studies. Therefore, we couldn’t rule out the possibility that defects in Salmonella clearance due to iNOS/NO inhibition may be caused by a complex combination of excess free zinc and overexpression of the zinc reservoir. To prove this hypothesis, further studies using the specific target, for example Mtfl/fliNOSfl/flLysMCre model might be needed to investigate the precision mechanism.

Author response image 3.

RT-qPCR analysis of mRNA encoding Nos2 in BMDMs after infected with Salmonella and Salmonella plus ZnSO4 (20 μM) for 4 h.

Reference:

Dlaska M, Weiss G. 1999. Central role of transcription factor NF-IL6 for cytokine and ironmediated regulation of murine inducible nitric oxide synthase expression. The Journal of Immunology. 162:6171-6177, PMID: 10229861

Kambe T, Tsuji T, Hashimoto A, Itsumura N. 2015. The physiological, biochemical, and molecular roles of zinc transporters in zinc homeostasis and metabolism. Physiological Reviews. 95:749-784. https://doi: 10.1152/physrev.00035.2014, PMID: 26084690

Schwarz MA, Lazo JS, Yalowich JC, Allen WP, Whitmore M, Bergonia HA, Tzeng E, Billiar TR, Robbins PD, Lancaster JR Jr, et al. 1995. Metallothionein protects against the cytotoxic and DNA-damaging effects of nitric oxide. Proceedings of the National Academy of Sciences of the United States of America. 92: 4452-4456. https://doi: 10.1073/pnas.92.10.4452, PMID: 7538671

Cong W, Niu C, Lv L, Ni M, Ruan D, Chi L, Wang Y, Yu Q, Zhan K, Xuan Y, Wang Y, Tan Y, Wei T, Cai L, Jin L. 2016. Metallothionein prevents age-associated cardiomyopathy via inhibiting NF-κB pathway activation and associated nitrative damage to 2-OGD. Antioxidants & Redox Signaling. 25: 936-952. https://doi: 10.1089/ars.2016.6648, PMID: 27477335

5) How does Zinc or TPEN supplementation to bacteria in LB medium affect the log growth of Salmonella?

We found that zinc supplementation at both low (20 µM) and high (640 µM) concentrations negatively effects Salmonella growth, especially during log phase and stationary phase in the broth culture medium, but not TPEN (20 µM) supplementation. These indicates that high zinc conditions occur at cellular levels such as within phagosomes (Botella et al., 2011) can limit bacterial growth.

Author response image 4.

Growth curve (optical density, OD 600 nm) of Salmonella in LB medium at different concentrations of ZnSO4 and/or TPEN. Bar graph indicating Salmonella growth at specific time points. Each value was expressed as mean of triplicates for each testing and data were determined using 2-tailed unpaired Student’s t-test. P<0.05, P<0.01, **P<0.001 and ns, not significant.

Reference:

Botella H, Peyron P, Levillain F, Poincloux R, Poquet Y, Brandli I, Wang C, Tailleux L, Tilleul S, Charrière GM, Waddell SJ, Foti M, Lugo-Villarino G, Gao Q, Maridonneau-Parini I, Butcher PD, Castagnoli PR, Gicquel B, de Chastellier C, Neyrolles O. 2011. Mycobacterial p(1)-type ATPases mediate resistance to zinc poisoning in human macrophages. Cell Host Microbe. 10:248-59. https://doi: 10.1016/j.chom.2011.08.006, PMID: 21925112

Reviewer #2 (Public Review):

This paper explores the importance of zinc metabolism in host defense against the intracellular pathogen Salmonella Typhimurium. Using conditional mice with a deletion of the Slc30a1 zinc exporter, the authors show a critical role for zinc homeostasis in the pathogenesis of Salmonella. Specifically, mice deficient in Slc30a1 gene in LysM+ myeloid cells are hypersusceptible to Salmonella infection, and their macrophages show alter phenotypes in response to Salmonella. The study adds important new information on the role metal homeostasis plays in microbe host interactions. Despite the strengths, the manuscript has some weaknesses. The authors conclude that lack of slc30a1 in macrophages impairs nos2-dependent anti-Salmonella activity. However, this idea is not tested experimentally. In addition, the research presented on Mt1 is preliminary. The text related to Figure 7 could be deleted without affecting the overall impact of the findings.

We thank the reviewer for his/her positive comments and constructive suggestions.

Reviewer #3 (Public Review):

Na-Phatthalung et al observed that transcripts of the zinc transporter Slc30a1 was upregulated in Salmonella-infected murine macrophages and in human primary macrophages therefore they sought to determine if, and how, Slc30a1 could contribute to the control of bacterial pathogens. Using a reporter mouse the authors show that Slc30a1 expression increases in a subset of peritoneal and splenic macrophages of Salmonella-infected animals. Specific deletion of Slc30a1 in LysM+ cells resulted in a significantly higher susceptibility of mice to Salmonella infection which, counter to the authors conclusions, is not explained by the small differences in the bacterial burden observed in vivo and in vitro. Although loss of Slc30a1 resulted in reduced iNOS levels in activated macrophages, the study lacks experiments that mechanistically link loss of NO-mediated bactericidal activity to Salmonella survival in Slc30a1 deficient cells. The additional deletion of Mt1, another zinc binding protein, resulted in even lower nitrite levels of activated macrophages but only modest effects on Salmonella survival. By combining genetic approaches with molecular techniques that measure variables in macrophage activation and the labile zinc pool, Na-Phattalung et al successfully demonstrate that Slc30a1 and metallothionein 1 regulate zinc homeostasis in order to modulate effective immune responses to Salmonella infection. The authors have done a lot of work and the information that Slc30a1 expression in macrophages contributes to control of Salmonella infection in mice is a new finding that will be of interest to the field. Whether the mechanism by which SLC30A1 controls bacterial replication and/or lethality of infection involves nitric oxide production by macrophages remains to be shown.

We very much appreciate the reviewer’s detailed evaluation and suggestions. The manuscript has been revised thoroughly according to the reviewer’s advice.

Author Response

Reviewer #1 (Public Review):

This work focuses on the mechanisms that underlie a previous observation by the authors that the type VI secretion system (T6SS) of a Pseudomonas chlororaphis (Pchl) strain can induce sporulation in Bacillus subtilis (Bsub). The authors bioinformatically characterize the T6SS system in Pchl and identify all the core components of the T6SS, as well as 8 putative effectors and their domain structures. They then show that the Pchl T6SS, and in particular its effector Tse1, is necessary to induce sporulation in Bsub. They demonstrate that Tse1 has peptidoglycan hydrolase activity and causes cell wall and cell membrane defects in Bsub. Finally, the authors also study the signaling pathway in Bsub that leads to the induction of sporulation, and their data suggest that cell wall damage may lead to the degradation of the anti-sigma factor RsiW, leading to activation of the extracellular sigma factor σW that causes increased levels of ppGpp. Sensing of high ppGpp levels by the kinases KinA and KinB may lead to phosphorylation of Spo0F, and induction of the sporulation cascade.

The findings add to the field's understanding of how competitive bacterial interactions work mechanistically and provide a detailed example of how bacteria may antagonize their neighbors, how this antagonism may be sensed, and the resulting defensive measures initiated.

While several of the conclusions of this paper are supported by the data, additional controls would bolster some aspects of the data, and some of the final interpretations are not substantiated by the current data.

• The Bsub signaling pathway that is proposed is intricate and extensive as shown in Fig 5A. However, the data supporting that is very sparse:

a) The authors show no data showing that the proteases PrsW and/or RasP, or the extracellular sigma factor σW are necessary, or that the cleavage of RsiW is needed, for induction of sporulation - this could presumably be tested using mutants of those genes.

It has been previously demonstrated that the proteases PrsW and/or RasP cleave RsiW under certain conditions such as alkaline-shock (Heinrich et al., 2009). In first place, PrsW cleaves RsiW and the resulting cleaved-RsiW serves as substrate to RasP. In the previous version of the manuscript, we already demonstrated that treatment with Tse1 causes damage to PG and delocalization of RsiW, however as the reviewer comments we did not show the participation of any of these proteases in the proposed signaling pathway. We have now generated single mutants in rsiW and prsW and they have been treated with Tse1. We have observed no variation in the levels of sporulation compared to untreated strains (Figure 1) a finding according to their suggested implication in the sporulation signaling pathway activated by Tse1. Positive controls, that is the single mutants grown at 37ºC, were still able to sporulate. This data has been added to Figure 6B in the new version of the manuscript.

As suggested by other reviewers, we have generated a sister plot of this figure showing the raw CFUs in each case. These data are included in Supplementary file 3. This experiment and the related figure have been incorporated into the new version of the manuscript.

Figure 1. A) Quantification of the percentage of sporulated Bsub, rsiW and prsW cells after treatment with purified Tse1 showing that rsiW and prsW single mutants are blind to the presence of Tse1. B) Cell density (CFUs/mL) of total (blue bars) and sporulated population (brown bars) of different Bacillus strains (Bsub, ∆rsiW and ∆prsW) untreated and treated with Tse1. Sporulation at 37ºC is shown as positive control in each strain. Statistical significance was assessed via t-tests. p value < 0.1, p value < 0.001, **p value < 0.0001.

Similarly, they don't demonstrate that the levels of ppGpp increase in the cell upon exposure to Pchl.

We have not been able to measure the levels of ppGpp, however, given that in the same proposed sporulation cascade the levels of different nucleotides are altered (Kriel et al., 2013, Tojo et al., 2013, López and Kolter, 2010), we have alternatively analyzed the levels of ATP using an ATP Determination Kit (Thermo, A22066). We have found that ATP levels increased by 3-fold in Bsub cells treated with Tse1 compared to untreated control cells. Consistently, no increase in ATP levels were observed in rsiW or prsW mutants treated with Tse1. We have incorporated all the raw luminescence data obtained for each sample and treatment in Figure 6-source data 1. This experiment, figures (Figure 6A in the new version of the manuscript) and description in “Materials and Methods” have been added to the new version of the manuscript.

c) There is some data showing that kinA and kinB mutants don't induce sporulation (Fig supplement 7A), but that is lacking the 'no attacker' control that would demonstrate an induction.

We have included in the new version of the manuscript the ‘no attacker’ control sporulation (%). The figure shows that the presence of Pchl strains induces the sporulation of all kinase mutants. This new data has been incorporated in Figure 6-figure supplement 1A in the new version of the manuscript.

d) There is some data showing that RsiW may be cleaved (Fig 5C, D), but that data would benefit from a positive control showing that the lack of YFP foci is seen in a condition where RsiW is known to be cleaved, as well as from a time-course showing that the foci are present prior to the addition of Tse1, and then disappear. As it is shown now, it is possible that the addition of Tse1 just blocks the production of RsiW or its insertion into the membrane (especially given the membrane damage seen). Further, there is no data that the disappearance of the YFP loci requires the proteases PrsW and /or RasP - such data would also support the idea that the disappearance is due to cleavage of RsiW.

Thank you for your useful suggestion. It is important to consider that we have not seen repression of the expression of genes that encode any of the two proteases on cells treated with Tse1 in our transcriptomics analysis. However, we agree that additional experiments would enhance the significance of our findings. We have repeated the whole experiment including a positive control to demonstrate that YFP foci disappears in a condition in which RsiW is known to be degraded by PrsW and RasP. Bacillus cells have been incubated in medium at pH 10 which provokes an alkaline shock that triggers RsiW cleavage (Asai, 2017; Heinrich et al., 2009). As shown in Fiugre 6D under this condition we also observed disappearance of YFP foci . We have also provided extra images with quantification of average signal from YFP-foci in Figure 6-figure supplement 2 .

• The entire manuscript suggests that T6SS is solely responsible for the induction of sporulation. While T6SS does appear to play a major part in explaining the sporulation induction seen, in the absence of 'no attacker' controls for Fig. 2A, it is impossible to see this. From the data shown in Fig. 2C, and figure supplement 2A, the 'no attacker' sporulation rate seems to be ~20%, while the rate is ~40% with Pchl strains lacking T6SS, suggesting that an additional factor may be playing a role.

This must be a misunderstanding of the message of this manuscript. The conceptual fundament of this study was settled in our previous manuscript (Molina-Santiago et al., 2019). We demonstrated that B. subtilis sporulated in the presence of P. chlororaphis. Interestingly, the overgrowth of P. chlororaphis over B. subtilis colony did not eliminate cells of B. subtilis, given that most of them were sporulated. The data we obtained strongly suggested that a functional T6SS was involved in the cellular response of Bacillus in the close cell to cell contact. In this new manuscript, we have explored this idea, and found that indeed, the T6SS of P. chlororaphis mobilized at least one effector, Tse1, which is able to trigger sporulation in Bacillus. Thus we did not conclude, and neither have done in this new study, that T6SS is the only factor expressed by P. chlororaphis responsible for sporulation activation in Bacillus. We have accordingly rephrased some sentences of the manuscript to clarify the proposed implication of T6SS in B. subtilis sporulation.

In addition, as mentioned above, we have included data of sporulation percentages in the absence of an attacker to better compare the induction of sporulation observed in the presence of the different Pchl strains and in the presence of Tse1.

Reviewer #2 (Public Review):

In a previous study, the authors showed that cell-cell contact with Pseudomonas chlororaphis induces sporulation in Bacillus subtilis. Here, the authors build on this finding and elucidate the mechanism behind this observation. They describe the enzymatic activity of a protein (Tse1) secreted by the type VI secretion system (T6SS) of P. chlororaphis (Pch), which partially degrades the peptidoglycan (PG) of targeted B. subtilis cells and triggers a signal cascade culminating in sporulation.

Most of the key conclusions of this paper (Tse1 being secreted by the T6SS and inducing sporulation in targeted cells) are well supported by the data. One conclusion (sporulation response being an anti-T6SS "defense" strategy) is not well supported by the data and should be removed or rephrased.

The authors elucidate the enzymatic activity of Tse1, a T6SS effector protein, in a genus (Pseudomonas) of great interest to microbiologists, and to researchers studying the T6SS specifically. They also carefully dissect the cellular response (signal cascade and sporulation) of an important model organism (B. subtilis; Bsub) specifically to exposure to Tse1. The results describing this cellular response contribute substantially to our understanding of how T6SS effector proteins interact with cells of Gram-positive species.

My only major concerns regard the interpretation of these results as sporulation being an adaptive and/or specific response to attacks by the T6SS. I outline my reasoning below.

• Interpretation of sporulation as a "defense" mechanism/strategy against the T6SS. In order for a phenotype X to be regarded as a "defense against Y" mechanism, it has to be shown that phenotype X (sporulation in response to Tse1) evolved - at least in part - for the purposes of increasing survival in the presence of Y (T6SS attacker). There are no experiments in this study comparing e.g. a sporulating Bsub with a non-sporulating Bsub, that would allow testing if sporulation increases survival. The experiments carefully describe the cellular response to Tse1, but no inference can be made with regards to this being adaptive for Bsub, or if it helps the cells survive against T6SS attacks, etc. A more parsimonious explanation would be that Tse1 happens to target the PG and causes envelope stress, triggering sporulation. So, it would be a general stress response that also happens to be triggered by T6SS. Now, some general (cell envelope) stress responses are known to be very effective at protecting against the T6SS. But in those instances, a beneficial effect for survival in the face of T6SS attacks has been shown in dedicated experiments. Purely observing a response to a T6SS effector, as this study does (very well), is not evidence that the response has evolved for the purpose of surviving T6SS attacks. Tucked away in the supplement (and briefly mentioned in the main text) is data on Bsub and Bacillus cereus, showing that i) cell densities of the sporulating Bsub and a sporulating B. cereus strain are not affected by an active T6SS, and ii) cell densities of an asporogenic B. cereus are slightly reduced by an active T6SS. However, the effect sizes of density reduction by the T6SS in the asporogenic B. cereus are minute (20x10^6 vs. ~50x10^6). In typical killing assays against e.g. gram-negative strains, a typical effect size for T6SS killing would be a several order of magnitude reduction in survival of the target strain when exposed to a T6SS attacker. Based on this dataset alone (Figure Suppl. 8), I would say that all three Bacillus strains are not experiencing any "fitness-relevant" killing by the T6SS, which is in line with the T6SS often being useless against gram-positives when it comes to killing. Hence, no claims about fitness benefits of sporulation in response to a T6SS attack, or this being a "defense mechanism/strategy" should be made in the manuscript.

Thanks for this interesting introductory and specific comments. We agree with the reviewer and have rephrased some sentences of the manuscript. Sporulation is not an adaptive or specific response of Bacillus to T6SS, indeed and as stated by reviewer 2, sporulation is a general stress response. It might happen that the way the manuscript was written, at some points, gave the wrong impression. In consequence we have rephrased some sentences. Nevertheless, in Figure supplement 8 (in the new version of the manuscript is Figure 6-figure supplement 3) we made a mistake during generation of the Figure. We have again done this experiment and we have generated a new and corrected chart that shows three orders of magnitude reduction in survival of the asporogenic B. cereus strain in competition with Pchl mutant strains compared to Pchl WT strain. These new findings show that the absence of sporulation ability leads to a severe reduction in survival of Bacillus cereus DSM 2302 population in competition with Pchl with an active T6SS compared to the survival in competition with Pchl hcp mutant. In this figure, it is also shown that Bacillus population also decreased in competition with tse1 mutant, demonstrating that Tse1 is responsible for killing Bacillus. However, there is a statistical difference in the survival of Bacillus competing with hcp or tse1 mutants. The increased survival of Bacillus in the interaction with tse1 strain compared to Bacillus-hcp competition, is suggestive of the ability of this strain to deliver additional T6SS-dependent toxins. This observation is in accordance to the data presented in Fig. 2B, which indicated that tse1 mutant has an active T6SS able to kill E. coli.

• Data supporting baseline "no competitor" sporulation rates being no different from those triggered by T6SS mutants is not convincing. For the data shown in Fig. 2A, a key comparison here would be to show baseline Bsub sporulation rates in absence of a competitor. This measurement is shown in Fig supplement 2A, and the value shown there (roughly 22% on average) appears to be much lower than the average T6SS mutant shown in Fig. 2A. The main text states that sporulation rates induced rate by the different T6SS mutants are "statistically" similar to the no-competitor baseline (L206/207). I am not convinced by this, since i) overall sporulation rates (incl of WT Pch) appear to have been lower in the experiment shown in supplement 2A, so a direct comparison between the no-competitor baseline and the data shown in Fig. 2A is not possible; and ii) hcp and tse1 mutants were tested in different experiments throughout the study, and sporulation rates appear to consistently hover around 30-40%, which is higher than the roughly 22% for "no competitor" depicted in Supplement Fig2A. I am focussing on this, because for the interpretation of the results, and the main narrative of the paper, knowing if "simply interacting with a T6SS-negative P. chlororaphis" induces some sporulation would make a big difference. One sentence in the discussion adds to my confusion about this: L464/465, "... a strain lacking paar (Δpaar) had an active T6SS that triggered sporulation comparably to Δhcp, ΔtssA, and Δtse1 strains", suggesting that the authors' claims that even strains lacking active T6SS trigger increased sporulation (which I would agree with, based on the data).

We understand the reviewer's comment that a direct comparison between the two figures is not correct due to fluctuations of the baseline sporulation rates between experiments. To solve this issue, we have added the baseline "no competitor" sporulation percentages in the experiments represented in Figure 2B in the new version of the manuscript.

Related with the sporulation provoked by a T6SS-negative P. chlororaphis, the reviewer is right. Bacillus sporulation occurs due to many external factors (abiotic and biotic stresses) so the presence of P. chlororaphis in the competition already has an effect on the sporulation percentage of B. subtilis. Accordingly, we have removed the statement on the sporulation rates induced by the different T6SS mutants are "statistically" similar to the no-competitor. However, our previous data (Molina-Santiago, Nat Comm 2019) and current findings convincedly demonstrate the relevance of the T6SS and, specifically the Tse1 toxin, in the induction of sporulation at least in the close cell to cell contact.

• Claim regarding "bacteriolytic activity" when tse1 is heterologously expressed in E. coli. The data supporting this claim (Fig2-supplement 2C) only shows a lower net population growth rate after induction of tse1 (truncated vs. non-truncated) expression. This could be caused by: slower growth (but no death), equal growth (with some death), or a combination of the two. The claim of "bacteriolytic" activity in E. coli is therefore not supported by this dataset.

We agree with the reviewer and we have decided to remove this figure and the experiment of “bacteriolytic activity” given that it does not contribute conceptually to the message of the manuscript.

I cannot comment in more detail on the validity of the biochemistry/enzymatic activity assays as these are not my area of expertise.

Reviewer #3 (Public Review):

The authors identify tse1, a gene located in the type 6 secretion system (T6SS) locus of the bacterium Pseudomonas chlororaphis, as necessary and sufficient for induction of Bacillus subtilis sporulation. The authors demonstrate that Tse1 is a hydrolase that targets peptidoglycan in the bacterial cell wall, triggering activation of the regulatory sigma factor sigma-w. The sporulation-inducing effects of sigma-w are dependent on the downstream presence of the sensor histidine kinases KinA and KinB. Overall, this is a well-structured paper that uses a combination of methods including bacterial genetics, HPCL, microscopy, and immunohistochemistry to elucidate the mechanism of action of Tse1 against B. subtilis peptidoglycan. There are some concerns regarding a few experimental controls that were not included/discussed and (in a few figures) the visual representation of the data could be improved. The structure of the manuscript and experiments is such that key questions are addressed in a logical flow that demonstrates the mechanisms described by the authors.

To begin, we have concerns regarding the sporulation assays and their results. The data should be presented as "Percent sporulation" or "Sporulation (%)" - not as a "sporulation rate": there is no kinetic element to any of these measurements, so no rate is being measured (be careful of this in the text as well, for instance near lines 204). More importantly, there is no data provided to indicate that changes in percent spores are not instead just the death of non-sporulated cells. For example, imagine that within a population of B. subtilis cells, 85% of the cells are vegetative and 15% are spores. If, upon exposure to tse1, a large proportion of the vegetative cells are killed (say, 80% of them), this could lead to an apparent increase in sporulation: from 15% for the untreated population to ~50% of the treated, but the difference would be entirely due to a change in the vegetative population, not due to a change in sporulation. The authors need to clearly describe how they conducted their sporulation assays (currently there is no information about this in the methods) as well as provide the raw data of the counts of vegetative cells for their assays to eliminate this concern.

Thanks for the suggestion. We have changed all the titles and data presented as “sporulation rate” by “sporulation (%)” or “sporulation percentage”. As also suggested by reviewer 2, we have included the raw data of the CFUs counts of total population and sporulated cells to show that there is no substantial change in the rate of death. Also, we have added a section in Material and Methods to specify how sporulation assays have been done. Quote text:

“Sporulation assays

Spots of bacteria were resuspended in 1 mL sterile distilled water. Then, serial dilutions were made and cultured in LB solid media for vegetative cells CFU counts. The same serial dilutions were further heated at 80ºC for 10 minutes to kill vegetative cells and immediately cultured again in LB solid media. Plates were grown overnight at 28 ºC and the resulting colonies were counted to calculate the percentage of Bsub sporulation (%). A list of raw CFUs (total and spore population) from all figures with sporulation percentage is shown in Supplementary file 3.”

A related concern is regarding the analysis of the kinases and the effects of their deletions on the impact of Tse1. Previous literature shows that the basal levels of sporulation in a B. subtilis kinA or a kinB mutant are severely defective relative to a wild-type strain; these mutants sporulate poorly on their own. Therefore, the data presented on Lines 394+ and the associated Supplemental Figure regarding the sporulation defects of these two mutants are not compelling for showing that these kinases are required for this effector to act. It is likely that simply missing these kinases would severely impact the ability of these strains to sporulate at all, irrespective of the presence of Tse1, and no discussion of this confounding concern is discussed.

Previous literature shows that mutation of kinases affects sporulation of B. subtilis. Histidine kinases KinA and KinB are the first responsible for initiation of sporulation cascade upon phosphorylation of spo0F. However, as shown in Figure 6-figure supplement 1A, single mutants in these kinases (ΔkinA, ΔkinB) still sporulate given that the phosphorylation cascade is controlled by numerous intermediaries and other histidine kinases that form a multicomponent phosphorelay (KinA-E). In this context, the sporulation of B. subtilis can be also triggered by KinC or KinD in the absence of KinA or KinB, as KinC/KinD can act directly on the master regulator of sporulation Spo0A (Burbulys et al., 1991; Wang et al., 2017).

In addition, as suggested by reviewer 1, we have added to Figure 6-figure supplement 1A of the new version of the manuscript, the sporulation percentage 'no competitor' control of each kinase mutant and B. subtilis WT. The results show that, as commented by the reviewer and also supported by literature, these mutants sporulate poorly on their own in the absence of an attacker (none). However, as shown in the figure, all kinase mutants increase the sporulation percentage in the presence of a competitor.

Another concern is regarding the statistical tests used in Figure 2. For statistical tests in A, B, and D, it should be stated whether a post-test was used to correct for multiple comparisons, and, if so, which post-test was used. to provide a stronger control comparison. For C, we suggest the inclusion of a mock control in addition to the two conditions already included (i.e., an extraction from an E. coli strain expressing the empty vector)

We have clarified the statistical tests used in Figure 2. Briefly, we have used one-way ANOVA followed by the Dunnett test in Figure 2A, B and D for the statistical analysis of the sporulation percentage of Bsub in competition with Pchl as control group. In relation to Figure 2C, it is not possible to add a mock control with a strain carrying the empty vector, because this is a suicide plasmid (pDEST17) unable to replicate in E. coli without chromosome integration.

An additional concern regarding controls is that there is an absence of loading controls for the immunoblot assays. In Figure 5D and all immunoblot assays, there is no mention of a loading control, which is a critical control that should be included.

In the previous version of the manuscript, we already included a loading control for Figure 5D in Figure supplement 7B, both for cell and for supernatant fractions. In the new version of the manuscript, the loading control of Figure 6E (in the previous version of the manuscript Figure 5D) is shown in Figure 6-figure supplement 2C. We have also included the original unedited gels and blot (Figure 6-figure supplement 2- source data 1 and Figure 6-figure supplement 2-source data 2).

Some of the visualizations could be improved to help the reader understand and appropriately interpret the data presented. For instance, in Figures 3 and 4 the scale bars are different across each of the Figure's imaging panels. These should be scaled consistently for better comparison. Additionally, the red false colorization makes the printed images difficult to see. Black-and-white would be easier to see and would not subtract from the images.

The reviewer is right. Scales bar equal 2 in Figure 3A, but the length of the bars was not the same. We have edited the images to have the same magnifications for better comparison.

In relation to Figure 4, we have changed the magnifications and now all the figures have the same scale bars and magnifications. In addition, we have added more images of broader fields in Figure 4-figure supplement 1 which were used to measure the percentage of permeabilized cells and to obtain the fluorescence intensity measures shown in Figure 4.

An additional weakness of the paper is that the RNA-seq data is not fully investigated, and there is an absence of methods included regarding the RNA-seq differential abundance analysis (it is mentioned on L379-380 but no information is provided in the methods). As stated by the authors, 58% of differentially regulated genes belonged to the sw regulon, but the other 42% of genes are not discussed, and will hopefully be a target of future investigations.

The methods section has been modified for a better explanation of the RNA-seq differential abundance analysis. Quote text: “The raw reads were pre-processed with SeqTrimNext (Falgueras et al., 2010) using the specific NGS technology configuration parameters. This pre-processing removes low-quality, ambiguous and low-complexity stretches, linkers, adapters, vector fragments, and contaminated sequences while keeping the longest informative parts of the reads. SeqTrimNext also discarded sequences below 25 bp. Subsequently, clean reads were aligned and annotated using the Bsub reference genome with Bowtie2 (Langmead and Salzberg, 2012) in BAM files, which were then sorted and indexed using SAMtools v1.484(Li et al., 2009). Uniquely localized reads were used to calculate the read number value for each gene via Sam2counts (https://github.com/vsbuffalo/sam2counts). Differentially expressed genes (DEGs) were analyzed via DEgenes Hunter, which provides a combined p value calculated (based on Fisher’s method) using the nominal p values provided by edgeR (Robinson et al., 2010) and DEseq2. This combined p value was adjusted using the Benjamini-Hochberg (BH) procedure (false discovery rate approach) and used to rank all the obtained DEGs. For each gene, combined p value < 0.05 and log2-fold change > 1 or < −1 were considered as the significance threshold”

Regarding the RNA-seq analysis, we are aware of the amount of information that can be extracted. Previous to filtering the information shown in the manuscript, we have done bioinformatic analysis trying to find a connection with the cellular response, that is increase of sporulation. Besides this, we had some observations but with no direct connection to sporulation, which would be interesting to pursue in future studies, but not for the clarity of this story (Figure 23 below). In any case, we are including the whole picture of the transcriptomics changes occurring in Bsub after treatment with Tse1. KEGG pathway analyses of genes differentially expressed showed induction of flagellar assembly and aminobenzoate degradation, nitrogen and amino acid metabolisms. Interestingly, fatty acid degradation and CAMP resistance pathways were also induced, probably related to changes suffered in the cell wall after the action of Tse1 toxin. On the other hand, synthesis and degradation of ketone bodies pathway was mostly repressed.

Figure 2. KEGG pathway analyses of genes differentially expressed occurring in Bsub after treatment with Tse1.

Another methodological concern in this paper is the limited details provided for the calculation of the permeabilization rate (Figure 4, L359, L662-664). It is not clear how, or if, cell density was controlled for in these experiments.

We agree with the reviewer and we have explained with more detail how the permeabilization rate was calculated. Quote text: “N=3 for Bsub treated with Tse1 and N=3 for untreated Bsub. N refers to the number of CLSM fields analyzed to calculate the number of permeabilized cells of the total of cells in the field”

Finally, one weakness of the paper is the broad conclusions that they draw. The authors claim that the mechanism of sporulation activation is conserved across Bacilli when the authors only test one B. subtilis and one B. cereus strain. They further argue (lines 469+) that Tse1 requires a PAAR repeat for its targeting, but do not provide direct evidence for this possibility.

We have reduced the tone of the final conclusion in order to specify that the activation of sporulation is a mechanism that can be found in different Bacillus species such as Bsub and Bcer. Related with the second appreciation, we have included a further explanation for this argument. Quote text: “As shown in Figure 2B, a paar mutant has an active T6SS able to kill E. coli. However, as shown in Figure 2A, we noticed that a paar mutant (which encodes tse1) is not able to trigger B. subtilis sporulation to a similar level than Pchl WT strain. Given that paar deletion apparently abolishes Tse1 secretion, we suggest that Tse1 is a PAAR-associated effector that requires a PAAR repeat domain protein to be targeted for secretion, thereby increasing Bacillus sporulation during contact with Pseudomonas cells (Cianfanelli et al., 2016; Hachani et al., 2014; Whitney et al., 2014)”.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Elkind et al. use a deep learning segmentation algorithm trained on detecting putative cell nuclei in mouse brains to count cells in the Allen Mouse Brain Connectivity Atlas. The Allen Mouse Brain Connectivity Atlas is a dataset compromising hundreds of mice brains. The authors use this increased statistical power for detecting differences in volume, cell count, and cell density between strains (C57BL/6J and FVB.CD1) as well as sex differences.

Both volume, cell count, and cell density are regularly used in neuroanatomy to normalize or benchmark results so having a large available dataset for others to compare their data would be a useful resource. The trained segmentation algorithm might also find utility in assays where investigators for one reason or another can't dedicate an entire labeled channel to count cell nuclei.

Nevertheless, because of technical reasons, I find the current work problematic.

We thank the Reviewer for acknowledging potential usefulness of our work, and the insightful, helpful comments. We believe this consideration has made our revised manuscript much stronger compared to the initial submission. We hope our revised version will also clear the Reviewer’s remaining doubts.

Major:

The authors make use of the "red" channel from the Allen Mouse Brain Connectivity Project (AMBCP). The AMBCP was acquired using two-photon tomography with the TissueCyte 1000 system (http://help.brain-map.org/download/attachments/2818171/Connectivity_Overview.pdf?version=2&modificationDate=1489022310670&api=v2). The sample is illuminated at 925 nm wavelength and the channel the authors describe as autofluorescence is collected through a 593/40 nm bandpass filter. The authors go on to describe their rationale for using this channel for quantifying cell nuclei:

"We noticed that the red (background) channel of STPT images, taken for the purpose of atlas alignment, typically features dark, round-like objects resembling cell nuclei. We had observed this phenomenon in our own imaging of mouse brains but found little more than anecdotal mentions of it in the literature8,9,10,11".

The authors here cite a Scientific Reports paper from 2021 with 11 citations, a Journal of Clinical Pathology paper from 2005 with 87 citations, and lastly a paper in Laboratory Investigation from 2016 with 41 citations. The authors completely fail to cite the work from Watt Webb's group (co-inventor of 2p microscopy) in PNAS from 2003 that entirely described the phenomena of native fluorescence by multiphoton- excitation (https://www.pnas.org/doi/10.1073/pnas.0832308100 ), citations so far: 1959 citations. This is either indicative of poor scholarship or an attempt to describe something as novel. Either way, the native fluorescence and second harmonic generation from multiphoton illumination are perfectly characterized by Webb and colleagues and they clearly show the differential effect on nucleosides, retinol, indoleamines, and collagen. This is also where the authors should have paid more attention to discrepancies in their own data when correlated to well-established cell nuclei markers (Murakami et al). The authors will note "black large spots" in the data at specific anatomical regions and structures, like the fornix and stria medullaris: https://connectivity.brain-map.org/projection/experiment/siv/263780729?imageId=263780960&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=15702&y=18833&z=5

which is not reproduced in for example the Allen Reference Atlas H&E staining: http://atlas.brain-map.org/atlas?atlas=1&plate=100960284#atlas=1&plate=100960284&resolution=4.19&x=5507.4000244140625&y=5903.39990234375&zoom=-2

In connection here notice the poor signal in the 2p "autofluorescence" within the paraventricular nucleus: https://connectivity.brain-map.org/projection/experiment/siv/263780729?imageId=263780960&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=15702&y=17833&z=6

and then compare it to the H&E staining: http://atlas.brain-map.org/atlas?atlas=1&plate=100960280#atlas=1&plate=100960276&resolution=1.50&x=5342.476283482143&y=5368.023856026786&zoom=0

These multiphoton-specific signals are especially pronounced in the pons and medulla which makes quantification especially dubious, which is even apparent simply from looking at Figure 1c in the manuscript.

We thank the Reviewer for the comments and sincerely apologize for missing the seminal work of Webb’s group. We included the former references for their specific mention or illustration of non-autofluorescent nuclei. We indeed entirely missed to address the underlying chemistry that Webb’s group beautifully characterized. We have added the following sentence in the Results section “Autofluorescence of STPT images displays cell nuclei” (red font for new sentence; Reference #15 corresponds to Zipfel et al.):

“We noticed that the red (background) channel of STPT images, taken for the purpose of atlas alignment, typically features dark, round-like objects resembling cell nuclei. This phenomenon was described in previous literature11,12,13,14. In particular, Zipfel et al. characterized the use of multiphoton-excited native florescence and second harmonic generation for the purpose of staining-free tissue imaging15.”

And mentioned the dependency of our method on the presence of intrinsically fluorescent molecules in the Discussion:

“The study has several limitations. First, the model is sensitive to the contrast between dark nuclei and autofluorescent surroundings, which can be limited by image quality and tissue composition. In particular, the staining-free approach depends on the presence of intrinsic molecular indicators such as NADH, retinol or collagen15, which may vary between cell or tissue components, even within the brain.”

We understand that more generally, the Reviewer’s major concern above was regarding the technical validity of our approach; that the segmentation based on small objects lacking autofluorescence, as evident in the STPT dataset, in fact corresponds to cells/nuclei.

In our initial Supplemental Figure 1 (in current version Figure 1—figure supplement 1) we provide technical validation of the method, by showing nuclear staining, and autofluorescence side-by-side, using epifluorescence microscopy. In our revision we now report appropriate statistical measures for this analysis (true positives, false positives, false negatives).

In addition, we performed the following two sets of validations –

(i) Technical validation of our staining-free quantification approach, by nuclear staining. We performed nuclear staining (Hoechst 33342) followed by STPT imaging of 9 female brains and trained a new deep neural network (DNN) to segment the resulting images (STPT was performed by TissueVision). Unfortunately, in STPT it is not technically possible to analyze nuclear staining and autofluorescence in the very same tissue. Therefore, we compared per-region density, cell count and volume of the nuclei-stained validation brains to our original DNN-based analysis of AMBCA brains. We show a correlation coefficient >0.99 for per-region cell count in AMBCA autofluorescence and our nuclear staining (and a similar correlation coefficient for volume). However, the number of cells in nuclear staining over the whole brain is 56% larger than in autofluorescence. Although we currently have no technically feasible way to prove this, one likely explanation for this discrepancy is the nature of the two signals the imaging detects; as positive (Hoechst fluorophore) or autofluorescence. Further, discrepancies between the two methods were notably higher in glial-rich tissues (e.g., CTX L1, midbrain, brainstem) – leading to the speculation that low-autofluorescent object-counts may be biased to detect neurons, rather than glia.

(ii) Independent validation of the biological findings – discussed further below. Regarding the specific concern of “black large spots” in the fornix and stria medullaris – we would like to emphasize that our DNN does not identify and segment dark regions like ventricles and tracks. We provide in the Author Response Image 1 three examples featuring “black large spots” of different shapes and size, with examples of the segmentation results as shown in Figures 1 and 2 of the manuscript. Note that colored circles, that appear as dots depending on magnification, are the objects that were detected and segmented by the DNN. In the Figure we demonstrate that (1) fiber tracts (incl. fornix, stria medullaris) are not segmented; (2) striatal patches (that are smaller still than the fiber tracts in question) are not segmented; and (3) putative blood vessels, appearing as elongated, black structures, are ignored by our DNN.

Author Response Image 1. How does the DNN deal with large black spots? Examples for fiber tracts, striatal patches, and blood vessels; adapted from Figures 1 and 2 in the manuscript. Note that dots/outlines represent segmented putative “nuclei” as detected by the model, colored by assigned region according to Allen Mouse Brain hierarchy. Example (1): fiber tracts (incl. fornix, stria medullaris) are not segmented. Example (2): Striasomes (patches in the striatum, that are smaller still than the fiber tracts in question) are not segmented, and the much smaller objects that are detected as putative nuclei are indicated by arrows. Example (3) putative blood vessels, appearing as elongated, black structures, are ignored by our DNN. Examples of the segmentation images were adapted from the manuscript’s Figure 1 to correspond to the STPT image featuring fiber tracts (and Striasomes/patches) was pointed out by the Reviewer.

Retrieved from: https://connectivity.brain-map.org/projection/experiment/siv/263780729?imageId=263780960&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=15702&y=18833&z=5.

Regarding the claim of problematic counting in brain stem regions, we agree, and had addressed this limitation in the manuscript’s Discussion (see below). We believe that our counting is valuable even if in some regions there is a significant systematic error: Most of the analyses in this study compare brain regions across individuals and thus systematic error is less impactful. In the revision, we nevertheless took care to validate and quantify the size of this effect. Briefly, we compared counting based on nuclear staining (Hoechst) from 9 STPT imaged brains, to our quantifications of non-autofluorescent objects. As expected, the ratio between these counts depends on the brain region, and accuracy is better in regions with high brightness, which are not on the border of the section (Figure 2—figure supplement 2). As for pons and medulla, the densities in our Hoechst quantifications are 43% and 60% higher than in our AMBCA analysis, respectively, yet rank order is kept in both.

We have revised the relevant sentences in the Discussion:

Original sentences: The study has several limitations. … In the hindbrain (pons, medulla), contrast was exceedingly weak, and we expect our quantifications in this region to strongly underestimate real cell densities, to an extent we cannot quantify.

Revised sentences: The study has several limitations. … In the hindbrain (pons, medulla), contrast was exceedingly weak, and we expect our quantifications in this region to be 66% of the value estimated by nuclear staining (Figure 2—figure supplement 2).

The authors here use the correlation on log-log coordinates between their data and that of Murakami et al to argue that the method has validity. However, the variance explained here is R^2 = 0.74 which is very poor given the log-log coordinates. A more valid metric would use linear coordinates and computing the ICC and interpret it according to established guidelines (e.g. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4913118/).

As mentioned by the Reviewer, Figure 2D compares Murakami et al. cell counts and ours, across all brain regions. The value “r=0.869” represents the correlation coefficient between the two vectors in log scale and not the R^2. We also now display the correlation coefficient for the linear scale, in which case p=0.98. As suggested by the Reviewer, we added ICC values between the two vectors in linear scale. Using 6 different forms (ICC – 1-1;1-k;C-1;C-k;A-1;A-k), the ICC values were 0.98-0.99, thus corresponding to an excellent agreement (ICC values are mentioned in legend of Figure 2).

Author Response Image 2 displays the revised Figure 2D (left), and the log value of the ratio between the AMBCA-based cell count and the Murakami-based value (right), as a function of region volume. The mean value across regions is zero, corresponding to similar cell counts in both methods. Indeed, there exist outlier regions, that may be attributed to either registration errors, different experimental protocols or may stem from the fact that the Murakami values are based on 3 brains, compared to hundreds of AMBCA brains.

Author Response Image 2. Correlation with cell counts in Murakami et al. Left, revised Figure 2D; Right, ratio between AMBCA-based cell counts and Murakami et al. counts, as a function of region volume  

In addition to the above concern, the authors argue that the large sample size of the AMBCP is what would enable them to find statistically significant small effect sizes that might have gone undetected in the literature. However, this argument falls flat once we examine some of the main findings the authors report. Although the authors do not directly report measures of dispersion we can estimate it from the figures and then arrive at the sample size needed to find the reported effect size. For example, the effect that describes ORBvl2/3 volume is larger in female mice compared to males would only require n=13 mice at the desired power of 0.8. Likewise, the sample size needed to detect the increased BST volume in male mice looks to be roughly n=16 mice at the desired power of 0.8. Both of these estimates are well within what is a reasonable sample size to expect in an ordinary study. This begs the question: why did the authors simply not verify some of their main findings in an independent sample obtained through traditional ways to quantify volume and cell density since it is well within reach? Such validation would strengthen the arguments of the paper.

We thank the reviewer for this comment and apologize. In the revised version we do report dispersion.

We would like to emphasize that due to our restricted time and resources, we decided to focus our experimental validation on the technical comparison of nuclear staining vs. autofluorescence-based segmentation, outlined above.

We then verified the biological findings from the initial cohort using C57BL/6J volume data from an additional 663 males vs.166 females on AMBCA. This independent cohort showed similar sexual dimorphism in the volume of MEA, BST and ORBvl2/3, as depicted in the following figure (panels A-D and also as new Figure 4—figure supplement 1).

We fully acknowledge the interesting issue raised on sample sizes required to detect our reported effect sizes. Therefore, we here also present the average p-value for sexual dimorphism in volumes of MEA, BST and ORBvl2/3, as a function of the sample size (panel E in Figure 4—figure supplement 1 of the revised manuscript). The Reviewer will note that the regions with largest effect size (MEA, BST) can be detected within more ordinary sample sizes, and indeed, MEA and BST dimorphism is evident in the literature. ORB dimorphism required much greater sample size; and our analysis (Figure 4) systematically detected many more dimorphic regions, in volume, density and count.

Reviewer #2 (Public Review):

This report describes a large-scale analysis of cell counts in mouse brains. The authors found that the Allen Mouse Connectivity project has a rich dataset for cell counting that is yet to be analyzed, and they developed methods to quantify cells in different nuclei. They go on to compare males vs females and two different strains. From this analysis, they found specific differences between male versus female brains, left versus right hemispheres, and C57BL/6 versus FVB.CD1 mice, especially with regard to cell counts and density.

Overall, the methodology is sound and the quality of the data seems high. In fact, this study uses >100 brains for the statistics, and this is one of the major strengths of this study. For researchers who are interested in interrogating the differences at the macroscopic level in brain structures, this study will be a great resource. For example, the manuscript contains an interesting finding that for most brain areas, females have larger volumes but fewer cell numbers.

We thank the Reviewer for these comments. We would like to mention that the revised version of the manuscript does not include a statement regarding BL6 female volume. We found a batch effect in the AMBCA experiments, mostly affecting the volume in their first batch (Figure 2—figure supplement 1B). That batch included mostly males, and had, for some reason, lower volume compared to all later experiments, which caused the volume differences. We emphasize that (1) the total number of cells did not show any batch effect (Figure 2—figure supplement 1C); (2) We normalized the volume and repeated the analysis. Aside the finding that females did not in fact have larger volumes, other main findings remained unchanged.

Reviewer #3 (Public Review):

Elkind et al. have devised a strategy to detect cells in whole brain samples of the large, publicly accessible Allen Mouse Brain Connectivity database. They put together an analysis pipeline to quantify cell numbers and -density as well as volumes for all annotated brain areas in these samples. This allowed them to make several important discoveries such as (1) strain-, sex- and hemisphere-specific differences in cell densities, (2) a large interindividual variability in cell numbers, and (3) an absence of linear scaling of cell count with volume, among others. The key strength of this work lies in its comprehensive analysis, the large sample size that the authors have drawn from (making their conclusions particularly robust), and the fact that they have made their analysis tools accessible. A weakness of the current manuscript is the dense layout and overplotting of several of the figures, and the lack of necessary information to understand them more easily. Another, conceptual weakness of using the autofluorescence channel for cell detection is that the identity (neuronal vs non-neuronal) of the underlying cells remains unresolved. Overall, however, I believe that this study has the potential to serve as a valuable reference point, and I would expect this work to have a lasting impact on quantitative studies of mouse brain cytoarchitecture.

We thank the Reviewer for these valuable comments. We have tried to minimize overplotting of figures and hopefully added all necessary information. For example, the revised manuscript presents more pared-down figures, with data labels omitted if they crowded the graphic. Instead, we provide the full data in Supplemental tables, and our online accessible GUI. We hope the reader will feel encouraged to both zoom the presented data, more deeply explore additional tables, and our online tool.

Regarding the question of cell types, we were unfortunately not able to provide a definitive answer, but our validation experiments provided some potential clues. For example, nuclear staining (Hoechst) uniformly detected 65% more cells than AMBCA autofluorescence quantification. And, in neuron-rich regions, the correspondence between nuclear staining and AMBCA autofluorescence was notably better than in glia-rich regions (e.g., CTX L1, midbrain, medulla). These discrepancies between the techniques may therefore point to an underlying difference in cell types composition – such that counting low-autofluorescent nuclei is biased to neurons.

In addition, however, the methods differ in their native physical properties; in that one detects presence of a fluorescent signal (e.g., the nuclear stain is detected beyond its focal plane), compared to the detection of the absence of a signal (which, in turn, is dependent on the presence of surrounding intrinsic fluorescent molecules). It is technically non-trivial to assess the extent to which these factors apply. We have added a clarification along these lines in the Discussion (below). We would further like to emphasize the nature of our study as a comparative, systematic analysis within this interesting cohort, rather than providing definitive cell counts – that we found to be greatly variable across the population.

“We further attempted to estimate the region-specific accuracy of our cell counting by comparing autofluorescence STPT with brain-wide imaging of nuclear-stained STPT. However, this comparison is technically nontrivial because of the native physical properties of direct staining vs. autofluorescence. For example, stained nuclei located off the focal plane may appear in the image, yet remain undetected by autofluorescence. In addition, tissue composition (e.g., cell types, extracellular matrix) may affect the imaged region. Indeed, in regions rich with non-neuronal cells the error of autofluorescent-based counting was larger compared to nuclear staining. Hence, one may speculate that autofluorescent-based detection is biased for neurons”

Author Response:

Reviewer #1 (Public Review):

Chakrabarti et al study inner hair cell synapses using electron tomography of tissue rapidly frozen after optogenetic stimulation. Surprisingly, they find a nearly complete absence of docked vesicles at rest and after stimulation, but upon stimulation vesicles rapidly associate with the ribbon. Interestingly, no changes in vesicle size were found along or near the ribbon. This would have indicated a process of compound fusion prior to plasma membrane fusion, as proposed for retinal bipolar cell ribbons. This lack of compound fusion is used to argue against MVR at the IHC synapse. However, that is only one form of MVR. Another form, coordinated and rapid fusion of multiple docked vesicles at the bottom of the ribbon, is not ruled out. Therefore, I agree that the data set provides good evidence for rapid replenishment of the ribbon-associated vesicles, but I do not find the evidence against MVR convincing. The work provides fundamental insight into the mechanisms of sensory synapses.

We thank the reviewer for the appreciation of our work and the constructive comments. As pointed out below, we now included this discussion (from line 679 onwards).

We wrote:

“This might reflect spontaneous univesicular release (UVR) via a dynamic fusion pore (i.e. ‘kiss and run’, (Ceccarelli et al., 1979), which was suggested previously for IHC ribbon synapses (Chapochnikov et al., 2014; Grabner and Moser, 2018; Huang and Moser, 2018; Takago et al., 2019) and/or and rapid undocking of vesicles (e.g. Dinkelacker et al., 2000; He et al., 2017; Nagy et al., 2004; Smith et al., 1998). In the UVR framework, stimulation by ensuing Ca2+ influx triggers the statistically independent release of several SVs. Coordinated multivesicular release (MVR) has been indicated to occur at hair cell synapses (Glowatzki and Fuchs, 2002; Goutman and Glowatzki, 2007; Li et al., 2009) and retinal ribbon synapses (Hays et al., 2020; Mehta et al., 2013; Singer et al., 2004) during both spontaneous and evoked release. We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

Reviewer #2 (Public Review):

Chakrabarti et al. aimed to investigate exocytosis from ribbon synapses of cochlear inner hair cells with high-resolution electron microscopy with tomography. Current methods to capture the ultrastructure of the dynamics of synaptic vesicle release in IHCs rely on the application of potassium for stimulation, which constrains temporal resolution to minutes rather than the millisecond resolution required to analyse synaptic transmission. Here the authors implemented a high-pressure freezing method relying on optogenetics for stimulation (Opto-HPF), granting them both high spatial and temporal resolutions. They provide an extremely well-detailed and rigorously controlled description of the method, falling in line with previously use of such "Opto-HPF" studies. They successfully applied Opto-HPF to IHCs and had several findings at this highly specialised ribbon synapse. They observed a stimulation-dependent accumulation of docked synaptic vesicles at IHC active-zones, and a stimulation-dependent reduction in the distance of non-docked vesicles to the active zone membrane; while the total number of ribbon-associated vesicles remained unchanged. Finally, they did not observe increases in diameter of synaptic vesicles proximal to the active zone, or other potential correlates to compound fusion - a potential mode of multivesicular release. The conclusions of the paper are mostly well supported by data, but some aspects of their findings and pitfalls of the methods should be better discussed.

We thank the reviewer for the appreciation of our work and the constructive comments.

Strengths:

While now a few different groups have used "Opto-HPF" methods (also referred to as "Flash and Freeze) in different ways and synapses, the current study implemented the method with rigorous controls in a novel way to specifically apply to cochlear IHCs - a different sample preparation than neuronal cultures, brain slices or C. elegans, the sample preparations used so far. The analysis of exocytosis dynamics of IHCs with electron microscopy with stimulation has been limited to being done with the application of potassium, which is not physiological. While much has been learned from these methods, they lacked time resolution. With Opto-HPF the authors were successfully able to investigate synaptic transmission with millisecond precision, with electron tomography analysis of active zones. I have no overall questions regarding the methodology as they were very thoroughly described. The authors also employed electrophysiology with optogenetics to characterise the optical simulation parameters and provided a well described analysis of the results with different pulse durations and irradiance - which is crucial for Opto-HPF.

Thank you very much.

Further, the authors did a superb job in providing several tables with data and information across all mouse lines used, experimental conditions, and statistical tests, including source code for the diverse analysis performed. The figures are overall clear and the manuscript was well written. Such a clear representation of data makes it easier to review the manuscript.

Thank you very much.

Weaknesses:

There are two main points that I think need to be better discussed by the authors.

The first refers to the pitfalls of using optogenetics to analyse synaptic transmission. While ChR2 provides better time resolution than potassium application, one cannot discard the possibility that calcium influx through ChR2 alters neurotransmitter release. This important limitation of the technique should be properly acknowledged by the authors and the consequences discussed, specifically in the context in which they applied it: a single sustained pulse of light of ~20ms (ShortStim) and of ~50ms (LongStim). While longer, sustained stimulation is characteristic for IHCs, these are quite long pulses as far as optogenetics and potential consequences to intrinsic or synaptic properties.

We thank the reviewer for pointing this out. We would like to mention that upon 15 min high potassium depolarization, the number of docked SVs only slightly increased as shown in Chakrabarti et al., 2018, EMBO rep and Kroll et al. 2020 JCS, but it was not statistically significant. In the current study, we report a similar phenomenon, but here light induced depolarization resulted in a more robust increase in the number of docked SVs.

To compare the data from the previous studies with the current study, we included an additional table 3 (line 676) now in the discussion with all total counts (and average per AZ) of docked SVs.

Furthermore, in response to the reviewers’ concern, we now discuss the Ca2+ permeability of ChR2 in addition to the above comparison to our previous studies that demonstrated very few docked SVs in the absence of K+ channel blockers and ChR2 expression in IHCs. We are not entirely certain, if the reviewer refers to potential dark currents of ChR2 (e.g. as an explanation for a depletion of docked vesicles under non-stimulated conditions) or to photocurrents, the influx of Ca2+ through ChR2 itself, and their contribution to Ca2+ concentration at the active zone.

However, regardless this, we consider it unlikely that a potential contribution of Ca2+ influx via ChR2 evokes SV fusion at the hair cell active zone.

First of all, we note that the Ca2+ affinity of IHC exocytosis is very low. As first shown in Beutner et al., 2001 and confirmed thereafter (e.g. Pangrsic et al., 2010), there is little if any IHC exocytosis for Ca2+ concentrations at the release sites below 10 µM. Two studies using CatCh (a ChR2 mutant with higher Ca2+ permeability than wildtype ChR2 (Kleinlogel et al., 2011; Mager et al., 2017) estimated a max intracellular Ca2+ increase below 10 µM, even at very negative potentials that promote Ca2+ influx along the electrochemical gradient or at high extracellular Ca2+ concentrations of 90 mM. In our experiments, IHCs were depolarized, instead, to values for which extrapolation of the data of Mager et al., 2017 indicate a submicromolar Ca2+ concentration. In addition, we and others have demonstrated powerful Ca2+ buffering and extrusion in hair cells (e.g. Tucker and Fettiplace, 1995; Issa and Hudspeth., 1996; Frank et al., 2009 Pangrsic et al., 2015). As a result, the hair cells efficiently clear even massive synaptic Ca2+ influx and establish a low bulk cytosolic Ca2+ concentration (Beutner and Moser, 2001; Frank et al., 2009). We reason that these clearance mechanisms efficiently counter any Ca2+ influx through ChR2. This will likely limit potential effects of ChR2 mediated Ca2+ influx on Ca2+ dependent replenishment of synaptic vesicles during ongoing stimulation.

We have now added the following in the discussion (starting in line 620):

“We note that ChR2, in addition to monovalent cations, also permeates Ca2+ ions and poses the question whether optogenetic stimulation of IHCs could trigger release due to direct Ca2+ influx via the ChR2. We do not consider such Ca2+ influx to trigger exocytosis of synaptic vesicles in IHCs. Optogenetic stimulation of HEK293 cells overexpressing ChR2 (wildtype version) only raises the intracellular Ca2+ concentration up to 90 nM even with an extracellular Ca2+ concentration of 90 mM (Kleinlogel et al., 2011). IHC exocytosis shows a low Ca2+ affinity (~70 µM, Beutner et al., 2001) and there is little if any IHC exocytosis for Ca2+ concentrations below 10 µM, which is far beyond what could be achieved even by the highly Ca2+ permeable ChR2 mutant (CatCh: Ca2+ translocating channelrhodopsin, Mager et al., 2017). In addition, we reason that the powerful Ca2+ buffering and extrusion by hair cells (e.g., Frank et al., 2009; Issa and Hudspeth, 1996; Pangršič et al., 2015; Tucker and Fettiplace, 1995) will efficiently counter Ca2+ influx through ChR2 and, thereby limit potential effects on Ca2+ dependent replenishment of synaptic vesicles during ongoing stimulation. “

The second refers to the finding that the authors did not observe evidence of compound fusion (or homotypic fusion) in their data. This is an interesting finding in the context of multivesicular release in general, as well as specifically for IHCs. While the authors discussed the potential for "kiss-and-run" and/or "kiss-and-stay", it would be valuable if they could discuss their findings further in the context of the field for multivesicular release. For example, the evidence in support of the potential of multiple independent release events. Further, as far as such function-structure optical-quick-freezing methods, it is not unusual to not capture fusion events (so-called omega-shapes or vesicles with fusion pores); this is largely because these are very fast events (less than 10 ms), and not easily captured with optical stimulation.

We agree with the reviewer that the discussion on MVR and UVR should be extended. We now added the following paragraph to the discussion from line 679 on:

“This might reflect spontaneous univesicular release (UVR) via a dynamic fusion pore (i.e. ‘kiss and run’, (Ceccarelli et al., 1979), which was suggested previously for IHC ribbon synapses (Chapochnikov et al., 2014; Grabner and Moser, 2018; Huang and Moser, 2018; Takago et al., 2019) and/or and rapid undocking of vesicles (e.g. Dinkelacker et al., 2000; He et al., 2017; Nagy et al., 2004; Smith et al., 1998). In the UVR framework, stimulation by ensuing Ca2+ influx triggers the statistically independent release of several SVs. Coordinated multivesicular release (MVR) has been indicated to occur at hair cell synapses (Glowatzki and Fuchs, 2002; Goutman and Glowatzki, 2007; Li et al., 2009) and retinal ribbon synapses (Hays et al., 2020; Mehta et al., 2013; Singer et al., 2004) during both spontaneous and evoked release. We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

Reviewer #3 (Public Review):

Precise methods were developed to validate the expression of channelrhodopsin in inner hair cells of the Organ of Corti, to quantify the relationship between blue light irradiance and auditory nerve fiber depolarization, to control light stimulation within the chamber of a high-pressure freezing device, and to measure with good precision the delay between stimulation and freezing of the specimen. These methods represent a clear advance over previous experimental designs used to study this synaptic system and are an initial application of rapid high-pressure freezing with freeze substitution, followed by high-resolution electron tomography (ET), to sensory cells that operate via graded potentials.

Short-duration stimuli were used to assess the redistribution of vesicles among pools at hair cell ribbon synapses. The number of vesicles linked to the synaptic ribbon did not change, but vesicles redistributed within the membrane-proximal pool to docked locations. No evidence was found for vesicle-to-vesicle fusion prior to vesicle fusion to the membrane, which is an important, ongoing question for this synapse type. The data for quantifying numbers of vesicles in membrane-tethered, non-tethered, and docked vesicle pools are compelling and important.

We thank the reviewer for the appreciation of our work and the constructive comments.

These quantifications would benefit from additional presentation of raw images so that the reader can better assess their generality and variability across synaptic sites.

The images shown for each of the two control and two experimental (stimulated) preparation classes should be more representative. Variation in synaptic cleft dimensions and numbers of ribbon-associated and membrane-proximal vesicles do not track the averaged data. Since the preparation has novel stimulus features, additional images (as the authors employed in previous publications) exhibiting tethered vesicles, non-tethered vesicles, docked vesicles, several sections through individual ribbons, and the segmentation of these structures, will provide greater confidence that the data reflect the images.

Thank you very much for pointing this out. We now included more details in supplemental figures and in the text.

Precisely, we added:

• More details about the morphological sub-pools (analysis and images):

  -We now show a sequence of images with different tethering states of membrane proximal SVs together with examples for docked and non-tethered SVs as we did in Chakrabarti et al., 2018 for each condition (Fig. 6-figure supplement 2, line 438). Moreover, we included for each condition additional information, we selected further tomograms, one per condition, and depict two additional virtual sections: Fig. 6-figure supplement 2.

  -Moreover, we present a more detailed quantification for the different morphological sub-pools: For the MP-SV pool, we analyzed the SV diameters and the distances to the AZ membrane and PD of different SV sub-pools separately, we now included this information in Fig. 7 For the RA-SVs, we analyzed in addition the morphological sub-pools and the SV diameters in the distal and the proximal ribbon part as done in Chakrabarti et al. 2018. We now added a new supplement figure (Fig. 7-figure supplement 2, line 558 and a supplementary file 2).

• We replaced the virtual section in panel 6D: In the old version, it appeared that the ribbon was contacting the membrane and we realized that this virtual section was not representative: actually, the ribbon was not directly contacting the AZ membrane, a presynaptic density was still visible adjacent to the docked SVs. To avoid potential confusion, we selected a different virtual section of the same tomogram and now indicated the presynaptic density also as graphical aid in Fig. 6.

The introduction raises questions about the length of membrane tethers in relation to vesicle movement toward the active zone, but this topic was not addressed in the manuscript.

We apologize for not stating it sufficiently clear, we now rephrased this sentence. We now wrote:

“…and seem to be organized in sub-pools based on the number of tethers and to which structure these tethers are connected. “

Seemingly quantification of this metric, and the number of tethers especially for vesicles near the membrane, is straightforward. The topic of EPSC amplitude as representing unitary events due to variation in vesicle volume, size of the fusion pore, or vesicle-vesicle fusion was partially addressed. Membrane fusion events were not evident in the few images shown, but these presumably occurred and could be quantified. Likewise, sites of membrane retrieval could also be marked. These analyses will broaden the scope of the presentation, but also contribute to a more complete story.

Regarding the presence/absence of membrane fusion events we agree with the reviewer that this should be clearly addressed in the MS. We would like to point out that we

(i) did not observe any omega shapes at the AZ membrane, which we also mention in the MS. We can also report that we could not see them in data sets from previous publications (Vogl et al., 2015, JCS; Jung et al., 2015, PNAS).

(ii) To be clear on our observations on potential SV-SV fusion events we now point out in the discussion from line 688ff:

“We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

Furthermore, we agree with the reviewer that a complete presentation of endo-exocytosis structural correlates is very important. However, we focused our study on exocytosis events and therefore mainly analyzed membrane proximal SVs at active zones.

Nonetheless, in response to the reviewer’s comment, we now included a quantification of clathrin-coated (CC) structures. We determined the appearance of CC vesicles (V) and CC invaginations within 0-500 nm away from the PD. We measured the diameter of the CCV, and their distance to the membrane and the PD. We only found very few CC structures in our tomograms (now added in a table to the result section (Supplementary file 1). Sites for endocytic membrane retrieval likely are in the peri-active zone area or even beyond. We did not observe obvious bulk endocytosis events that were connected to the AZ membrane. However, we do observe large endosomal like vesicles that we did not quantify in this study. More details were presented in two of our previous studies: Kroll et al., 2019 and 2020, however, under different stimulation conditions.

Overall, the methodology forms the basis for future studies by this group and others to investigate rapid changes in synaptic vesicle distribution at this synapse.

Reviewer #4 (Public Review):

This manuscript investigates the process of neurotransmitter release from hair cell synapses using electron microscopy of tissue rapidly frozen after optogenetic stimulation. The primary finding is that in the absence of a stimulus very few vesicles appear docked at the membrane, but upon stimulation vesicles rapidly associate with the membrane. In contrast, the number of vesicles associated with the ribbon and within 50 nm of the membrane remains unchanged. Additionally, the authors find no changes in vesicle size that might be predicted if vesicles fuse to one-another prior to fusing with the membrane. The paper claims that these findings argue for rapid replenishment and against a mechanism of multi-vesicular release, but neither argument is that convincing. Nonetheless, the work is of high quality, the results are intriguing, and will be of interest to the field.

We thank the reviewer for the appreciation of our work and the constructive comments.

1) The abstract states that their results "argue against synchronized multiquantal release". While I might agree that the lack of larger structures is suggestive that homotypic fusion may not be common, this is far from an argument against any mechanisms of multi-quantal release. At least one definition of synchronized multiquantal release posits that multiple vesicles are fusing at the same time through some coordinated mechanism. Given that they do not report evidence of fusion itself, I fail to see how these results inform us one way or the other.

We agree with the reviewer that the discussion on MVR and UVR should be extended. It is important to point out that we do not claim that the evoked release is mediated by one single SV. As discussed in the paper (line 672), we consider that our optogenetic stimulation of IHCs triggers the release of more than 10 SVs per AZ. This falls in line with the previous reports of several SVs fusing upon stimulation. This type of evoked MVR is probably mediated by the opening of Ca2+ channels in close proximity to each SV Ca2+ sensor. We indeed sometimes observed more than one docked SV per AZ upon long optogenetic stimulation. This could reflect that possibility. However, given the absence of large structures directly at the ribbon or the AZ membrane that could suggest the compound fusion of several SVs prior or during fusion, we argue against compound MVR release at IHCs. As mentioned above, we added to the discussion (from line 679 onwards).

We wrote:

“This might reflect spontaneous univesicular release (UVR) via a dynamic fusion pore (i.e. ‘kiss and run’, (Ceccarelli et al., 1979), which was suggested previously for IHC ribbon synapses (Chapochnikov et al., 2014; Grabner and Moser, 2018; Huang and Moser, 2018; Takago et al., 2019) and/or and rapid undocking of vesicles (e.g. Dinkelacker et al., 2000; He et al., 2017; Nagy et al., 2004; Smith et al., 1998). In the UVR framework, stimulation by ensuing Ca2+ influx triggers the statistically independent release of several SVs. Coordinated multivesicular release (MVR) has been indicated to occur at hair cell synapses (Glowatzki and Fuchs, 2002; Goutman and Glowatzki, 2007; Li et al., 2009) and retinal ribbon synapses (Hays et al., 2020; Mehta et al., 2013; Singer et al., 2004) during both spontaneous and evoked release. We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

2) The complete lack of docked vesicles in the absence of a stimulus followed by their appearance with a stimulus is a fascinating result. However, since there are no docked vesicles prior to a stimulus, it is really unclear what these docked vesicles represent - clearly not the RRP. Are these vesicles that are fusing or recently fused or are they ones preparing to fuse? It is fine that it is unknown, but it complicates their interpretation that the vesicles are "rapidly replenished". How does one replenish a pool of docked vesicles that didn't exist prior to the stimulus?

In response to the reviewers’ comment, we would like to note that we indeed reported very few docked SVs in wild type IHCs at resting conditions without K+ channel blockers in Chakrabarti et al. EMBO Rep 2018 and in Kroll et al., 2020, JCS. In both studies, a solution without TEA and Cs was used for the experiments (resting solution Chakrabarti: 5 mM KCl, 136.5 mM NaCl, 1 mM MgCl2, 1.3 mM CaCl2, 10 mM HEPES, pH 7.2, 290 mOsmol; control solution Kroll: 5.36 mM KCl, 139.7 mM NaCl, 2 mM CaCl2, 1 mM MgCl2, 0.5 mM MgSO4, 10 mM HEPES, 3.4 mM L-glutamine, and 6.9 mM D-glucose, pH 7.4). Similarly, our current study shows very few docked SVs in the resting condition even in the presence of TEA and Cs. Based on the results presented in ‘Response to reviewers Figure 1’, we assume that the scarcity of docked SVs under control conditions is not due to depolarization induced by a solution containing 20 mM TEA and 1 mM Cs but is rather representative for the physiological resting state of IHC ribbon synapses. Upon 15 min high potassium depolarization, the number of docked SVs only slightly increased as shown in Chakrabarti et al., 2018 and Kroll et al. 2020, but it was not statistically significant. In the current study, we report a similar phenomenon, but here depolarization resulted in a more robust increase in the number of docked SVs.

To compare the data from the previous studies with the current study, we included an additional table 3 (line 676) now in the discussion with all total counts (and average per AZ) of docked SVs.

Author Response

eLife assessment:

This study addresses whether the composition of the microbiota influences the intestinal colonization of encapsulated vs unencapsulated Bacteroides thetaiotaomicron, a resident micro-organism of the colon. This is an important question because factors determining the colonization of gut bacteria remain a critical barrier in translating microbiome research into new bacterial cell-based therapies. To answer the question, the authors develop an innovative method to quantify B. theta population bottlenecks during intestinal colonization in the setting of different microbiota. Their main finding that the colonization defect of an acapsular mutant is dependent on the composition of the microbiota is valuable and this observation suggests that interactions between gut bacteria explains why the mutant has a colonization defect. The evidence supporting this claim is currently insufficient. Additionally, some of the analyses and claims are compromised because the authors do not fully explain their data and the number of animals is sometimes very small.

Thank you for this frank evaluation. Based on the Reviewers’ comments, the points raised have been addressed by improving the writing (apologies for insufficient clarity), and by the addition of data that to a large extent already existed or could be rapidly generated. In particularly the following data has been added:

1. Increase to n>=7 for all fecal time-course experiments

2. Microbiota composition analysis for all mouse lines used

3. Data elucidating mechanisms of SPF microbiome/ host immune mechanisms restriction of acapsular B. theta

4. Short- versus long-term recolonization of germ-free mice with a complete SPF microbiota and assessment of the effect on B. theta colonization probability.

5. Challenge of B. theta monocolonized mice with avirulent Salmonella to disentangle effects of the host inflammatory response from other potential explanations of the observations.

6. Details of all inocula used

7. Resequencing of all barcoded strains

Additionally, we have improved the clarity of the text, particularly the methods section describing mathematical modeling in the main text. Major changes in the text and particularly those replying to reviewers comment have been highlighted here and in the manuscript.

Reviewer #1 (Public Review):

The study addresses an important question - how the composition of the microbiota influences the intestinal colonization of encapsulated vs unencapsulated B. theta, an important commensal organism. To answer the question, the authors develop a refurbished WITS with extended mathematical modeling to quantify B. theta population bottlenecks during intestinal colonization in the setting of different microbiota. Interestingly, they show that the colonization defect of an acapsular mutant is dependent on the composition of the microbiota, suggesting (but not proving) that interactions between gut bacteria, rather than with host immune mechanisms, explains why the mutant has a colonization defect. However, it is fairly difficult to evaluate some of the claims because experimental details are not easy to find and the number of animals is very small. Furthermore, some of the analyses and claims are compromised because the authors do not fully explain their data; for example, leaving out the zero values in Fig. 3 and not integrating the effect of bottlenecks into the resulting model, undermines the claim that the acapsular mutant has a longer in vivo lag phase.

We thank the reviewer for taking time to give this details critique of our work, and apologies that the experimental details were insufficiently explained. This criticism is well taken. Exact inoculum details for experiment are now present in each figure (or as a supplement when multiple inocula are included). Exact microbiome composition analysis for OligoMM12, LCM and SPF microbiota is now included in Figure 2 – Figure supplement 1.

Of course, the models could be expanded to include more factors, but I think this comment is rather based on the data being insufficiently clearly explained by us. There are no “zero values missing” from Fig. 3 – this is visible in the submitted raw data table (excel file Source Data 1), but the points are fully overlapped in the graph shown and therefore not easily discernable from one another. Time-points where no CFU were recovered were plotted at a detection limit of CFU (50 CFU/g) and are included in the curve-fitting. However, on re-examination we noticed that the curve fit was carried out on the raw-data and not the log-normalized data which resulted in over-weighting of the higher values. Re-fitting this data does not change the conclusions but provides a better fit. These experiments have now been repeated such that we now have >=7 animals in each group. This new data is presented in Fig. 3C and D and Fig. 3 Supplement 2.

Limitations:

1) The experiments do not allow clear separation of effects derived from the microbiota composition and those that occur secondary to host development without a microbiota or with a different microbiota. Furthermore, the measured bottlenecks are very similar in LCM and Oligo mice, even though these microbiotas differ in complexity. Oligo-MM12 was originally developed and described to confer resistance to Salmonella colonization, suggesting that it should tighten the bottleneck. Overall, an add-back experiment demonstrating that conventionalizing germ-free mice imparts a similar bottleneck to SPF would strengthen the conclusions.

These are excellent suggestions and have been followed. Additional data is now presented in Figure 2 – figure supplement 8 showing short, versus long-term recolonization of germ-free mice with an SPF microbiota and recovering very similar values of beta, to our standard SPF mouse colony. These data demonstrate a larger total niche size for B. theta at 2 days post-colonization which normalizes by 2 weeks post-colonization. Independent of this, the colonization probability, is already equivalent to that observed in our SPF colony at day 2 post-colonization. Therefore, the mechanisms causing early clonal loss are very rapidly established on colonization of a germ-free mouse with an SPF microbiota. We have additionally demonstrated that SPF mice do not have detectable intestinal antibody titers specific for acapsular B. theta. (Figure 2 – figure supplement 7), such that this is unlikely to be part of the reason why acapsular B. theta struggles to colonize at all in the context of an SPF microbiota. Experiments were also carried to detect bacteriophage capable of inducing lysis of B. theta and acapsular B. theta from SPF mouse cecal content (Figure 2 – figure supplement 7). No lytic phage plaques were observed. However, plaque assays are not sensitive for detection of weakly lytic phage, or phage that may require expression of surface structures that are not induced in vitro. We can therefore conclude that the restrictive activity of the SPF microbiota is a) reconstituted very fast in germ-free mice, b) is very likely not related to the activity of intestinal IgA and c) cannot be attributed to a high abundance of strongly lytic bacteriophage. The simplest explanation is that a large fraction of the restriction is due to metabolic competition with a complex microbiota, but we cannot formally exclude other factors such as antimicrobial peptides or changes in intestinal physiology.

2) It is often difficult to evaluate results because important parameters are not always given. Dose is a critical variable in bottleneck experiments, but it is not clear if total dose changes in Figure 2 or just the WITS dose? Total dose as well as n0 should be depicted in all figures.

We apologized for the lack of clarity in the figures. Have added panels depicting the exact inoculum for each figure legend (or a supplementary figure where many inocula were used). Additionally, the methods section describing how barcoded CFU were calculated has been rewritten and is hopefully now clearer.

3) This is in part a methods paper but the method is not described clearly in the results, with important bits only found in a very difficult supplement. Is there a difference between colonization probability (beta) and inoculum size at which tags start to disappear? Can there be some culture-based validation of "colonization probability" as explained in the mathematics? Can the authors contrast the advantages/disadvantages of this system with other methods (e.g. sequencing-based approaches)? It seems like the numerator in the colonization probability equation has a very limited range (from 0.18-1.8), potentially limiting the sensitivity of this approach.

We apologized for the lack of clarity in the methods. This criticism is well taken, and we have re-written large sections of the methods in the main text to include all relevant detail currently buried in the extensive supplement.

On the question of the colonization probability and the inoculum size, we kept the inoculum size at 107 CFU/ mouse in all experiments (except those in Fig.4, where this is explicitly stated); only changing the fraction of spiked barcoded strains. We verified the accuracy of our barcode recovery rate by serial dilution over 5 logs (new figure added: Figure 1 – figure supplement 1). “The CFU of barcoded strains in the inoculum at which tags start to disappear” is by definition closely related to the colonization probability, as this value (n0) appears in the calculation. Note that this is not the total inoculum size – this is (unless otherwise stated in Fig. 4) kept constant at 107 CFU by diluting the barcoded B. theta with untagged B. theta. Again, this is now better explained in all figure legends and the main text.

We have added an experiment using peak-to-trough ratios in metagenomic sequencing to estimate the B. theta growth rate. This could be usefully employed for wildtype B. theta at a relatively early timepoint post-colonization where growth was rapid. However, this is a metagenomics-based technique that requires the examined strain to be present at an abundance of over 0.1-1% for accurate quantification such that we could not analyze the acapsular B. theta strain in cecum content at the same timepoint. These data have been added (Figure 3 – figure supplement 3). Note that the information gleaned from these techniques is different. PTR reveals relative growth rates at a specific time (if your strain is abundant enough), whereas neutral tagging reveals average population values over quite large time-windows. We believe that both approaches are valuable. A few sentences comparing the approaches have been added to the discussion.

The actual numerator is the fraction of lost tags, which is obtained from the total number of tags used across the experiment (number of mice times the number of tags lost) over the total number of tags (number of mice times the number of tags used). Very low tag recovery (less than one per mouse) starts to stray into very noisy data, while close to zero loss is also associated with a low-information-to-noise ratio. Therefore, the size of this numerator is necessarily constrained by us setting up the experiments to have close to optimal information recovery from the WITS abundance. Robustness of these analyses is provided by the high “n” of between 10 and 17 mice per group.

4) Figure 3 and the associated model is confusing and does not support the idea that a longer lag-phase contributes to the fitness defect of acapsular B.theta in competitive colonization. Figure 3B clearly indicates that in competition acapsular B. theta experiences a restrictive bottleneck, i.e., in competition, less of the initial B. theta population is contributed by the acapsular inoculum. There is no need to appeal to lag-phase defects to explain the role of the capsule in vivo. The model in Figure 3D should depict the acapsular population with less cells after the bottleneck. In fact, the data in Figure 3E-F can be explained by the tighter bottleneck experienced by the acapsular mutant resulting in a smaller acapsular founding population. This idea can be seen in the data: the acapsular mutant shedding actually dips in the first 12-hours. This cannot be discerned in Figure 3E because mice with zero shedding were excluded from the analysis, leaving the data (and conclusion) of this experiment to be extrapolated from a single mouse.

We of course completely agree that this would be a correct conclusion if only the competitive colonization data is taken into account. However, we are also trying to understand the mechanisms at play generating this bottleneck and have investigated a range of hypotheses to explain the results, taking into account all of our data.

Hypothesis 1) Competition is due to increased killing prior to reaching the cecum and commencing growth: Note that the probability of colonization for single B. theta clones is very similar for OligoMM12 mouse single-colonization by the wildtype and acapsular strains. For this hypothesis to be the reason for outcompetition of the acapsular strain, it would be necessary that the presence of wildtype would increase the killing of acapsular B. theta in the stomach or small intestine. The bacteria are at low density at this stage and stomach acid/small intestinal secretions should be similar in all animals. Therefore, this explanation seems highly unlikely

Hypothesis 2) Competition between wildtype and acapsular B. theta occurs at the point of niche competition before commencing growth in the cecum (similar to the proposal of the reviewer). It is possible that the wildtype strain has a competitive advantage in colonizing physical niches (for example proximity to bacteria producing colicins). On the basis of the data, we cannot exclude this hypothesis completely and it is challenging to measure directly. However, from our in vivo growth-curve data we observe a similar delay in CFU arrival in the feces for acapsular B. theta on single colonization as in competition, suggesting that the presence of wildtype (i.e., initial niche competition) is not the cause of this delay. Rather it is an intrinsic property of the acapsular strain in vivo,

Hypothesis 3) Competition between wildtype and acapsular B. theta is mainly attributable to differences in growth kinetics in the gut lumen. To investigate growth kinetics, we carried our time-courses of fecal collection from OligoMM12 mice single-colonized with wildtype or acapsular B. theta, i.e., in a situation where we observe identical colonization probabilities for the two strains. These date, shown now in Figure 3 C and D and Figure 3 – figure supplement 2, show that also without competition, the CFU of acapsular B. theta appear later and with a lower net growth rate than the wildtype. As these single-colonizations do not show a measurable difference between the colonization probability for the two strains, it is not likely that the delayed appearance of acapsular B. theta in feces is due to increased killing (this would be clearly visible in the barcode loss for the single-colonizations). Rather the simplest explanation for this observation is a bona fide lag phase before growth commences in the cecum. Interestingly, using only the lower net growth rate (assumed to be a similar growth rate but increased clearance rate) produces a good fit for our data on both competitive index and colonization probability in competition (Figure 3, figure supplement 5). This is slightly improved by adding in the observed lag-phase (Figure 3). It is very difficult to experimentally manipulate the lag phase in order to directly test how much of an effect this has on our hypothesis and the contribution is therefore carefully described in the new text.

Please note that all data was plotted and used in fitting in Fig 3E, but “zero-shedding” is plotted at a detection limit and overlayed, making it look like only one point was present when in fact several were used. This was clear in the submitted raw data tables. To sure-up these observations we have repeated all time-courses and now have n>=7 mice per group.

5) The conclusions from Figure 4 rely on assumptions not well-supported by the data. In the high fat diet experiment, a lower dose of WITS is required to conclude that the diet has no effect. Furthermore, the authors conclude that Salmonella restricts the B. theta population by causing inflammation, but do not demonstrate inflammation at their timepoint or disprove that the Salmonella population could cause the same effect in the absence of inflammation (through non-inflammatory direct or indirect interactions).

We of course agree that we would expect to see some loss of B. theta in HFD. However, for these experiments the inoculum was ~109 CFUs/100μL dose of untagged strain spiked with approximately 30 CFU of each tagged strain. Decreasing the number of each WITS below 30 CFU leads to very high variation in the starting inocula from mouse-to-mouse which massively complicates the analysis. To clarify this point, we have added in a detection-limit calculation showing that the neutral tagging technique is not very sensitive to population contractions of less than 10-fold, which is likely in line with what would be expected for a high-fat diet feeding in monocolonized mice for a short time-span.

This is a very good observation regarding our Salmonella infection data. We have now added the fecal lipocalin 2 values, as well as a group infected with a ssaV/invG double mutant of S. Typhimurium that does not cause clinical grade inflammation (“avirulent”). This shows 1) that the attenuated S. Typhimurium is causing intestinal inflammation in B. theta colonized mice and 2) that a major fraction of the population bottleneck can be attributed to inflammation. Interestingly, we do observe a slight bottleneck in the group infected with avirulent Salmonella which could be attributable either to direct toxicity/competition of Salmonella with B. theta or to mildly increased intestinal inflammation caused by this strain. As we cannot distinguish these effects, this is carefully discussed in the manuscript.

6) Several of the experiments rely on very few mice/groups.

We have increased the n to over 5 per group in all experiments (most critically those shown in Fig 3, Supplement 5). See figure legends for specific number of mice per experiment.

Reviewer #2 (Public Review):

The goal of this study was to understand population bottlenecks during colonization in the context of different microbial communities. Capsular polysaccharide mutants, diet, and enteric infection were also used paired to short-term monitoring of overall colonization and the levels of specific strains. The major strength of this study is the innovative approach and the significance of the overall research area.

The first major limitation is the lack of clear and novel insight into the biology of B. theta or other gut bacterial species. The title is provocative, but the experiments as is do not definitively show that the microbiota controls the relative fitness of acapsular and wild-type strains or provide any mechanistic insights into why that would be the case. The data on diet and infection seem preliminary. Furthermore, many of the experiments conflict with prior literature (i.e., lack of fitness difference between acapsular and wild-type strain and lack of impact of diet) but satisfying explanations are not provided for the lack of reproducibility.

In line with suggestions from Reviewer 1, the paper has undergone quite extensive re-writing to better explain the data presented and its consequences. Additionally, we now explicitly comment on apparent discrepancies between our reported data and the literature – for example the colonization defect of acapsular B. theta is only published for competitive colonizations, where we also observe a fitness defect so there is no actual conflict. Additionally, we have calculated detection limits for the effect of high-fat diet and demonstrate that a 10-fold reduction in the effective population size would not be robustly detected with the neutral tagging technique such that we are probably just underpowered to detect small effects, and we believe it is important to point out the numerical limits of the technique we present here. Additionally for the Figure 4 experiments, we have added data on colonization/competition with an avirulent Salmonella challenge giving some mechanistic data on the role of inflammation in the B. theta bottleneck.

Another major limitation is the lack of data on the various background gut microbiotas used. eLife is a journal for a broad readership. As such, describing what microbes are in LCM, OligoMM, or SPF groups is important. The authors seem to assume that the gut microbiota will reflect prior studies without measuring it themselves.

All gnotobiotic lines are bred as gnotobiotic colonies in our isolator facility. This is now better explained in the methods section. Additionally, 16S sequencing of all microbiotas used in the paper has been added as Figure 2 – figure supplement 1.

I also did not follow the logic of concluding that any differences between SPF and the two other groups are due to microbial diversity, which is presumably just one of many differences. For example, the authors acknowledge that host immunity may be distinct. It is essential to profile the gut microbiota by 16S rRNA amplicon sequencing in all these experiments and to design experiments that more explicitly test the diversity hypotheses vs. alternatives like differences in the membership of each community or other host phenotypes.

This is an important point. We have carried out a number of experiments to potentially address some issues here.

1) We carried out B. theta colonization experiments in germ-free mice that had been colonized by gavage of SPF feces either 1 day prior to colonization of 2 weeks prior to colonization. While the shorter pre-colonization allowed B. theta to colonize to a higher population density in the cecum, the colonization probability was already reduced to levels observed in our SPF colony in the short pre-colonization. Therefore, the factors limiting B. theta establishment in the cecum are already established 1-2 days post-colonization with an SPF microbiota (Figure 2 - figure supplement 8). 2) We checked for the presence of secretory IgA capable of binding to the surface of live B. theta, compared to a positive control of a mouse orally vaccinated against B. theta. (Fig. 2, Supplement 7) and could find no evidence of specific IgA targeting B. theta in the intestinal lavages of our SPF mouse colony. 3) We isolated bacteriophage from the intestine of SPF mice and used this to infect lawns of B. theta wildtype and acapsular in vitro. We could not detect and plaque-forming phage coming from the intestine of SPF mice (Figure 2 – figure supplement 7).

We can therefore exclude strongly lytic phage and host IgA as dominant driving mechanisms restricting B. theta colonization. It remains possible that rapidly upregulated host factors such as antimicrobial peptide secretion could play a role, but metabolic competition from the microbiota is also a very strong candidate hypothesis. The text regarding these experiments has been slightly rewritten to point out that colonization probability inversely correlates with microbiota complexity, and the mechanisms involved may involve both direct microbe-microbe interactions as well as host factors.

Given the prior work on the importance of capsule for phage, I was surprised that no efforts are taken to monitor phage levels in these experiments. Could B. theta phage be present in SPF mice, explaining the results? Alternatively, is the mucus layer distinct? Both could be readily monitored using established molecular/imaging methods.

See above: no plaque-forming phage could be recovered from the SPF mouse cecum content. The main replicative site that we have studied here, in mice, is the cecum which does not have true mucus layers in the same way as the distal colon and is upstream of the colon so is unlikely to be affected by colon geography. Rather mucus is well mixed with the cecum content and may behave as a dispersed nutrient source. There is for sure a higher availability of mucus in the gnotobiotic mice due to less competition for mucus degradation by other strains. However, this would be challenging to directly link to the B. theta colonization phenotype as Muc2-deficient mice develop intestinal inflammation.

The conclusion that the acapsular strain loses out due to a difference of lag phase seems highly speculative. More work would be needed to ensure that there is no difference in the initial bottleneck; for example, by monitoring the level of this strain in the proximal gut immediately after oral gavage.

This is an excellent suggestion and has been carried out. At 8h post-colonization with a high inoculum (allowing easy detection) there were identical low levels of B. theta in the upper and lower small intestine, but more B. theta wildtype than B. theta acapsular in the cecum and colon, consistent with commencement of growth for B. theta wildtype but not the acapsular strain at this timepoint. We have additionally repeated the single-colonization time-courses using our standard inoculum and can clearly see the delayed detection of acapsular B. theta in feces even in the single-colonization state when no increased bottleneck is observed. This can only be reasonably explained by a bona fide lag-phase extension for acapsular B. theta in vivo. These data also reveal and decreased net growth rate of acapsular B. theta. Interestingly, our model can be quite well-fitted to the data obtained both for competitive index and for colonization probability using only the difference in net growth rate. Adding the (clearly observed) extended lag-phase generates a model that is still consistent with our observations.

Another major limitation of this paper is the reliance on short timepoints (2-3 days post colonization). Data for B. theta levels over 2 weeks or longer is essential to put these values in context. For example, I was surprised that B. theta could invade the gut microbiota of SPF mice at all and wonder if the early time points reflect transient colonization.

It should be noted that “SPF” defines microbiota only on missing pathogens and not on absolute composition. Therefore, the rather efficient B. theta colonization in our SPF colony is likely due to a permissive composition and this is likely to be not at all reproducible between different SPF colonies (a major confounder in reproducibility of mouse experiments between institutions. In contrast the gnotobiotic colonies are highly reproducible). We do consistently see colonization of our SPF colony by wildtype B. theta out to at least 10 days post-inoculation (latest time-point tested) at similar loads to the ones observed in this work, indicating that this is not just transient “flow-through” colonization. Data included below:

For this paper we were very specifically quantifying the early stages of colonization, also because the longer we run the experiments for, the more confounding features of our “neutrality” assumptions appear (e.g., host immunity selecting for evolved/phase-varied clones, within-host evolution of individual clones etc.). For this reason, we have used timepoints of a maximum of 2-3 days.

Finally, the number of mice/group is very low, especially given the novelty of these types of studies and uncertainty about reproducibility. Key experiments should be replicated at least once, ideally with more than n=3/group.

For all barcode quantification experiments we have between 10 and 17 mice per group. Experiments for the in vivo time-courses of colonization have been expanded to an “n” of at least 7 per group.

Author Response:

Reviewer #1 (Public Review):

The authors report the generation of a mesoscale excitatory projectome from the ventrolateral prefrontal cortex (vlPFC) in the macaque brain by using AAV2/9-CaMKIIa-Tau-GFP labeling and imaging with high-throughput serial two-photon tomography. They present a novel data pipeline that integrates the STP data with macroscopic dMRI data from the same brain in a common 3D space, achieving a direct comparison of the two tracing methods. The analysis of the data revealed an interesting discrepancy between the high resolution STP data and the lower resolution dMRI data with respect to the extent of the frontal lobe projection through the inferior fronto-occipital fasciculus (IFOF) - the longest associative axon bundle in the human brain.

The authors report the generation of a mesoscale excitatory projectome from the ventrolateral prefrontal cortex (vlPFC) in the macaque brain by using AAV2/9-CaMKIIa-Tau-GFP labeling and imaging with high-throughput serial two-photon tomography. They also present a novel data pipeline that integrates the STP data with macroscopic dMRI data from the same brain in a common 3D space, achieving a direct comparison of the two tracing methods. Overall the paper can serve as a how to example for analyzing large non-human primate brain data, though some parts of the paper can be improved and the interpretation of the data should also be further strengthened.

We thank the reviewer for his positive evaluation of our manuscript.

The methodological part should include more detail on image acquisition - speed of imaging, pixel residence time, total time for data acquisition of a single brain and data sizes. Also the time and hardware needed for the computational analysis should be included, including the registration to the common reference and the running time for the machine learning predictions - this should also include the F score for the axon detection.

We thank the reviewer for pointing out these vital issues. We have added these technical details in the resubmitted manuscript.

“High x-y resolution (0.95 μm/pixel) serial 2D images were acquired in the coronal plane at a z-interval of 200 μm across the entire macaque brain. The scanning time of a single field-of-view which contains 1024 by 1024 pixels was 1.629 s (i.e., pixel residence time was ~1.6 μs), as resulted in a continuous ~1 month scanning and ~5 TB STP tomography data for a single monkey brain.”

“The data analysis was undertaken on a compute cluster with a 3.1 - 3.3 GHz 248 core CPU, 2.8 T of RAM, and 17472 CUDA cores.”

“The total computational time for the machine learning predictions in one macaque brain was ~ 1.5 months.”

“To evaluate overall classifier performance, the precision–recall F measure, also called F-score, was computed by using additional four labeled images as test sets. Higher accuracy performance achieved by the classifier often yield higher F-scores (94.41% ± 1.99%, mean ± S.E.M.).”

“For registration to the 3D common space, it took half an hour approximately.”

The discrepancy between the high resolution STP data and the lower resolution dMRI data with respect to the extent of the frontal lobe projection through the inferior fronto-occipital fasciculus seems puzzling. One would expect that the STP data would reveal more detail not less.. One possibility is that the Tau-GFP does not diffuse throughout the full axon arborization of the PFC neurons, resulting in a technical artifact. Can this be excluded to support the functional significance of the current data?

We thank the reviewer for raising this important issue. We apologize for not providing sufficient details of the IFOF debate due to limited space and causing confusion. We have added literature background of the IFOF debate to the section of Introduction (also recommended by Reviewer #2). Thanks to the comments by Reviewer #2, the present finding provides direct support for the speculation that the IFOF of macaque monkeys may not exist in a mono-synaptic way.

The AAV construct encoding cytoskeletal GFP (Tau-GFP) was used here to label all processes of the infected neuron, including axons and synaptic terminals. About 3 weeks of post-surgery survival time are usually sufficient to label intracerebral circuits in rodents (Lanciego and Wouterlood, 2020). We have extended the survival time to 2-3 months in order to achieve adequate labeling of axonal fibers and terminals in macaques.

Regarding the extent of Tau-GFP diffuse, the STP images and high-resolution confocal microscopic analysis further showed differences in the morphology of axon fibers that populate the route and terminals of these axon fibers. Consistent with previous reports (Fuentes-Santamaria et al., 2009; Watakabe and Hirokawa, 2018), the axon fibers were thin and formed bouton-like varicosities in the terminal regions (MD, Figure 2—figure supplement 7D; caudate, Figure 2—figure supplement 7J; PFC, Figure 1—figure supplement 5A-D). Those results indicate that the Tau-GFP has reached axonal terminals.

References:

Fuentes-Santamaria V, Alvarado JC, McHaffie JG, Stein BE (2009) Axon Morphologies and Convergence Patterns of Projections from Different Sensory-Specific Cortices of the Anterior Ectosylvian Sulcus onto Multisensory Neurons in the Cat Superior Colliculus. Cereb Cortex 19:2902-2915.

Lanciego JL, Wouterlood FG (2020) Neuroanatomical tract-tracing techniques that did go viral. Brain Struct Funct 225:1193-1224.

Watakabe A, Hirokawa J (2018) Cortical networks of the mouse brain elaborate within the gray matter. Brain Struct Funct 223:3633-3652.

Reviewer #2 (Public Review):

The authors utilized viral vectors as neural tracers to delineate the connectivity map of the macaque vlPFC at the axonal level. There are three main goals of this study: 1) determine an effective viral vector for tract-tracing in the macaque brain, 2) delineate the detailed map of excitatory vlPFC projections to the rest of the brain, and 3) compare vlPFC connectivity between tracing and tractography results.

We thank the reviewer for his/her constructive comments, to which we respond below.

Accordingly, my comments are organized around each aim:

1) This study demonstrates the advantage of viral tracing technique in targeting neuron type-specific pathways. The authors conducted injection experiments with three types of viral vectors and found success of AAV in labeling long-distance connections without causing fatal neurotoxicity in the monkey. This success extends the application of AAV from rodents to nonhuman primates. The fact that AAV specifically targets glutamatergic neurons makes it advantageous for mapping excitatory projections.

Although the labeling efficacy of each viral vector type is described in the text, Fig. 2 does not present a clear comparison across viral vectors, despite such comparison for a thalamic injection in Fig. 2S. Without a comparable graph to Fig. 2E, it is unclear to what extent the VSV and lentivirus failed in labeling long-distance pathways.

We thank the reviewer for the helpful suggestion. As suggested, we have added three new figures as Supplementary materials in the revised manuscript.

Figure 2—figure supplement 2. Expression of GFP using VSV-△G injected into MD thalamus of the macaque brain. (A) GFP-labeled neurons were found in the MD thalamus ~5 days after injection of VSV-△G encoding Tau-GFP. (B) A magnified view illustrating the morphology of GFP-labeled neurons in the area outlined with a white box in (A). (C) Higher magnification view of GFP-positive axons.

Figure 2—figure supplement 3. Expression of GFP using lentivirus injected into MD thalamus of the macaque brain. (A) Lentivirus construct was injected into the macaque thalamus and examined for transgene expression after ~9 months. (B) High power views of the dotted rectangle in panel A. (C) Magnified view of panel B. Note the presence of GFP-positive cells.

Figure 2—figure supplement 4. Expression of GFP using AAV2/9 injected into MD thalamus of the macaque brain. (A) GFP-labeled axons were observed in the subcortical regions ~42 days after injection of AAV2/9 encoding Tau-GFP in MD thalamus. The inset shows the injection site in MD thalamus. Two dashed line boxes enclose the regions of interest: frontal white matter and ALIC, whose GFP signal are magnified in (B) and (C), respectively. (D) Higher magnification view of GFP-positive axons.

2) The authors quantified connectivity strength by the GFP signal intensity using a machine-learning algorithm. Both the quantitative approach and the resulting excitatory projection map are important contributions to advancing our knowledge of vlPFC connectivity.

However, several issues with the analysis lead to concerns about the connectivity result. First, the strength measure is based on axonal patterns in the terminal fields (which the authors refer to as "axon clusters"), detected by a machine-learning algorithm (page 25, lines 11-13). However, the actual synaptic connections are the small dot-looking signals in the background. These "green dots" are boutons on the dendritic trees. The density of boutons rather than the passing fibers reflects the density of synapses. The brief method description does not mention how the boutons are quantified, and it is unclear whether the signal was treated as the background noise and filtered out. Second, it is difficult for the reader to assess the robustness of the vlPFC connectivity patterns, due to these issues: i) It is unclear how many injection cases were used to generate the result reported in the subsection "Brain-wide excitatory projectome of vlPFC in macaques". The text mentions a singular "injection site" (page 8, line 12) and Fig. 4 shows a single site. However, there are three cases listed in Table 1. Is the result an average of all three cases? ii) Relatedly, it is unclear in which anatomical area the injection was placed for each case. Table 1 lists the site as "vlPFC" for all three cases, while the vlPFC contains areas 44, 45 and 12l. These areas have different projection patterns documented in the tract tracing literature. If different areas were injected in the three cases, they should be reported separately. iii) It is hard to compare the projection patterns with those reported in the literature. Conventionally, tract tracing studies report terminal fields by showing original labeling patterns in both cortical and subcortical regions without averaging within divided areas (see e.g. Petrides & Pandya, 2007, J Neurosci). It is hard to compare Fig. 3 with previous tract tracing studies to assess its robustness.

We thank the reviewer for his/her constructive comments, to which we respond below.

1). We appreciate the reviewer’s comment and sincerely apologize for not explaining this point clearly in our previous submission. The major concern is whether the axonal varicosities were likely to be treated as the background noise and removed by mistake. In fact, the dot-looking autofluorescence rather than the axonal varicosities were reduced through a machine-learning algorithm in segmentation. Hence we have provided new results and updated the “Materials and Methods” and “Discussion” sections in the revision accordingly.

“Fluorescent images of primate (Abe et al., 2017) brain often contain high-intensity dot-looking background signal caused by accumulation of lipofuscin. Thanks to the broad emission spectrum of lipofuscin, dot-looking background and GFP-positive axonal varicosities are easily distinguishable from each other. For instance (Figure 1—figure supplement 4), axonal varicosities can be selectively excited in green channel, while dot-looking background lipofuscin usually present in both green channel and red channel. During quantitative analysis, a machine learning algorithm was adopted to reliably segment the GFP labelled axonal fibers including axonal varicosities, and remove the lipofuscin background (Arganda-Carreras et al., 2017; Gehrlach et al., 2020).”

“One recent study compared results of terminal labelling using Synaptophysin-EGFP-expressing AAV (specifically labelling synaptic endings) with the cytoplasmic EGFP AAV (labelling axon fibers and synaptic endings). There was high correspondence between synaptic EGFP and cytoplasmic EGFP signals in target regions (Oh et al., 2014). Thus, we relied on quantifying GFP-positive pixels (containing signals from both axonal fibers and terminals) rather than the number of synaptic terminals, similarly done in recent reports (Oh et al., 2014; Gehrlach et al., 2020).”

Figure 1—figure supplement 4. Difference between axonal varicosities and dot-looking background. STP images (A-D) and high-resolution confocal images (E-H) were acquired in green channel and the red channel. Synaptic terminals (indicated by white arrows) can be specifically excited in green channel, while dot-looking background lipofuscin (indicated by yellow arrows) can be visualized both in green channel and red channel. (C and G) No colocalization was found between axonal varicosities and dot-looking background. Axonal varicosities were easily distinguished from dot-looking background in the merged image. (D and H) The dot-looking autofluorescence rather than the axonal varicosities was reduced through a machine-learning algorithm.

References:

Abe H, Tani T, Mashiko H, Kitamura N, Miyakawa N, Mimura K, Sakai K, Suzuki W, Kurotani T, Mizukami H, Watakabe A, Yamamori T, Ichinohe N (2017) 3D reconstruction of brain section images for creating axonal projection maps in marmosets. J Neurosci Methods 286:102-113.

Arganda-Carreras I, Kaynig V, Rueden C, Eliceiri KW, Schindelin J, Cardona A, Sebastian Seung H (2017) Trainable Weka Segmentation: a machine learning tool for microscopy pixel classification. Bioinformatics 33:2424-2426.

Gehrlach DA, Weiand C, Gaitanos TN, Cho E, Klein AS, Hennrich AA, Conzelmann KK, Gogolla N (2020) A whole-brain connectivity map of mouse insular cortex. Elife 9.

Oh SW et al. (2014) A mesoscale connectome of the mouse brain. Nature 508:207-214.

2.1) We apologize for causing these confusions due to insufficient description in the main text. Now we have revised the description of the “Materials and Methods” section accordingly. Furthermore, we have made both the whole-brain serial two-photon data and high-resolution diffusion MRI data freely available to the community, as allows researchers in the field to perform further analyses that we have not done in the current study.

“Three samples were injected with AAV in vlPFC, and two of them were able to be imaged with STP. Unfortunately, one sample became “loose” and fell off from the agar block after several weeks of imaging. So, the quantitative results were not shown in Figure 3.”

2.2) We apologize for insufficient description of the precise location of the injection sites. We have revised the description of “Materials and Methods” section and provided a new figure to clarify the exact location of the injection sites.

“Figure 3-4 and Figure 4—figure supplement 2-4 were derived from sample #8 with infected area in 45, 12l and 44 of vlPFC. Figure 1—figure supplement 6 was derived from sample #7 with infected area in 12l and 45 of vlPFC.”

Figure 1—figure supplement 6. Representative fluorescent images showing injection site and major tracts of sample #7. (A) STP image of the injection site in vlPFC are shown overlaid with the monkey brain template (left hand side), mainly spanning areas 12l and 45a. (B) Confocal image of the AAV infected neurons (indicated by white arrows). (C-F) Representative confocal images of major tracts originating from vlPFC.

2.3) We agree with the reviewer that most tract tracing studies report terminal fields by showing original labeling patterns. Several recent studies report the total volume of segmented GFP-positive pixels (Oh et al., 2014) or percentage of total labeled axons (Do et al., 2016; Gehrlach et al., 2020) to represent the connectivity strength, and other studies provide the projection density as well (Hunnicutt et al., 2016). We have provided both percentage of total labeled axons (Figure 3C right panel), projection density (Figure 3C left panel) and representative original fluorescent images (Figure. 4, Figure 4—figure supplement 2 and Figure 4—figure supplement 4) to demonstrate our projection data at different dimensions.

References:

Do JP, Xu M, Lee SH, Chang WC, Zhang S, Chung S, Yung TJ, Fan JL, Miyamichi K, Luo L, Dan Y (2016) Cell type-specific long-range connections of basal forebrain circuit. Elife 5.

Gehrlach DA, Weiand C, Gaitanos TN, Cho E, Klein AS, Hennrich AA, Conzelmann KK, Gogolla N (2020) A whole-brain connectivity map of mouse insular cortex. Elife 9.

Hunnicutt BJ, Jongbloets BC, Birdsong WT, Gertz KJ, Zhong H, Mao T (2016) A comprehensive excitatory input map of the striatum reveals novel functional organization. Elife 5.

Oh SW et al. (2014) A mesoscale connectome of the mouse brain. Nature 508:207-214.

3) Using the ground-truth from tract tracing to validate tractography results is a timely problem and this study showed promising consistency and discrepancy between the two modalities. Especially, the discrepancy between tracing and tractography data on the IFOF termination brings critical insights into a potential cross-species difference. The finding that IFOF does not reach the occipital cortex provides important support for the speculation that IFOF may not exist in monkeys (for a context of the IFOF debate see Schmahmann & Pandya, 2006, pp 445-446).

I have minor concerns regarding the statistical robustness of the tracing-tractography comparison. The authors compared the vlPFC-CC-contralateral tract instead of a global connectivity pattern without justification. Why omitting other major tracts that connect with vlPFC? In addition, the results are shown for only one monkey, while two monkeys went through both tracer injection and dMRI scans. It is unclear how the results were chosen or whether the data were averaged.

We apologize for not describing it clearly. The STP images were acquired in the coronal plane with high x-y resolution (0.95 μm/pixel), while the z resolution was relatively low (200 μm). The axonal connection information along z axis may be lost due to the present step size (relatively large) such that it is technically demanding to reconstruct the axonal density maps in sagittal or horizontal plane. Therefore, we focused on the vlPFC-CC-contralateral tract traveling along the coronal plane when quantifying the similarity coefficients along the anterior-posterior axis of the whole macaque brain, and omitted the tracts that were shown as dots in the coronal plane. We have revised it in the resubmitted manuscript.

“GFP projection and probabilistic tract were plotted with the Dice coefficients and Pearson coefficients (R) along the anterior-posterior axis of the whole macaque brain. The Dice coefficients and Pearson coefficients were higher in dense projection regions, especially for the vlPFC-CC-contralateral tract (Figure 6A). To carry out a proof-of-principle investigation, we focused on the vlPFC-CC-contralateral tract that was reconstructed in 3D space by using STP and dMRI data, respectively.”

With regard to the demonstration of dMRI data, we apologize for not making it clear in previous version. We have already revised Figure 6 and Figure 7 so that dMRI scans from different macaque monkeys were shown separately.

Figure 6. Comparison of vlPFC connectivity profiles by STP tomography and diffusion tractography. (A) Percentage of projection, Probabilistic tracts, Dice coefficients and Pearson coefficients (R) were plotted along the anterior-posterior axis in the macaque brain. Blue and red colors indicate results of two dMRI data sets acquired from different macaque monkeys. (B, C) 3D visualization of the fiber tracts issued from the injection site in vlPFC to corpus callosum to the contralateral vlPFC by STP tomography and diffusion tractography. (D-F) Representative coronal slices of the diffusion tractography map and the axonal density map along the vlPFC-CC-contralateral tract, overlaid with the corresponding anatomical MR images. (G-J) GFP-labeled axon images as marked in Figure 6F were shown with magnified views. (H, J) correspond to high magnification images of the white boxes indicated in G and I, both of which presented a great deal of details about axonal morphology.

Figure 7. Illustration of the inferior fronto-occipital fasciculus by diffusion tractography and STP. (A) The fiber tractography of IFOF (lateral view). Two inclusion ROIs at the external capsule (pink) and the anterior border of the occipital lobe (purple) were used and shown on the coronal plane. The IFOF stems from the frontal lobe, travels along the lateral border of the caudate nucleus and external/extreme capsule, forms a bowtie-like pattern and anchors into the occipital lobe. (B) The reconstructed traveling course of IFOF based on vlPFC projectome was shown in 3D space. (C) The Szymkiewicz-Simpson overlap coefficients between 2D coronal brain slices of the dMRI-derived IFOF tract and vlPFC projections were plotted along the anterior-posterior axis of the macaque brain. Blue and red colors indicate results of two dMRI data sets acquired from different macaque monkeys. Four cross-sectional slices (D-G) along the IFOF tracts were arbitrarily chosen to demonstrate the spatial correspondence between the diffusion tractography and axonal tracing of STP images. (D-G) The detected GFP signals (green) of vlPFC projectome and the IFOF tracts (red) obtained by diffusion tractography were overlaid on anatomical MRI images, with a magnified view of the box area. Evidently there was no fluorescent signal detected in the superior temporal area where the dMRI-derived IFOF tract passes through (G).

Author Response

Reviewer #1 (Public Review):

This is a well-executed study using cutting-edge proteomics analysis to characterize muscle tissue from a genetically diverse mouse population. The use of only females in the study is a serious limitation that the authors acknowledge. The statistical methods, including protein quantification, QTL mapping, and trait correlation analysis are appropriate and include corrections for multiple testing. One concern is that missense variants, if they occur in peptides used to quantify proteins, could lead to false-positive signatures of low abundance (see lines 123-127). The experimental validation and deep dive into UFMylation provide some confidence in the reliability of other associations that can be mined from these data. The authors have provided a web-based tool for exploring the data.

We thank the reviewer for these very positive comments and for reviewing the manuscript.

We agree the quantification of peptides containing missense variants could confound quantification at the protein level. This is an important consideration when there are only a few peptides identified for a specific protein. However, in our data the average number of peptides used to quantify the 14 proteins containing missense-associated pQTLs was ~68 peptides/protein (lowest was 5 peptides for FGB and highest 703 peptides for NEB).

In the case of EPHX1, we quantified 15 peptides (Figure R1A). We identified a peptide adjacent to R338 spanning amino acids 339-347. As such, mutation of R338C would prevent trypsin from cleavage resulting in the missense peptide not being identified and may lead to false-positive signatures of low abundance as suggested by the reviewer. To investigate this, we re-quantified EPHX1 relative protein abundance with or without the peptide spanning 339-347 for each genotype (Figure R1B). This made little difference to protein quantification and EPHX1 abundance was still significantly lower following mutation of R338C (AA genotype). In fact, quantification at the peptide-level revealed 12 out of the remaining 14 peptides were also significantly lower in AA genotype (data not shown).

Although we agree this a very important consideration, we are mindful of the length of the article and feel including these data would not significantly improve the manuscript. We therefore request to not include these data as it would detract from the main findings of the paper focused on phenotypic associations and validation of UFMylation as a regulator of muscle function.

Figure 1R. (A) Identified peptides from EPHX1 mapped onto primary amino acid sequence highlighting the missense mutation induced by SNP rs32746574 that was associated to EPHX1 protein levels by pQTL analysis. (B) Relative quantification of EPHX1 between the two genotypes of SNP rs32746574 with and without the peptide neighboring the missense mutation (amino acids 339-347) (**p<0.001, students t-test)