Author Response

eLife Assessment:

This manuscript follows the still unanswered concept of 'original antigenic sin' and shows the existence of a 24-year periodicity of the immune response against influenza H3N2. The valuable work suggests a long-term periodicity of individual antibody response to influenza A (H3N2) within a city. But, to substantiate their argument, the authors would need to provide additional supporting data.

Thank you for your comments. We have performed additional analyses and included those results in the revision to support our findings.

Specifically, we included a sensitivity analyses that predicting phases by fitting models with 35- and 6-years periodicity, which were found to provide poorer predictions than the 24-year periodicity used in our main results (Figure 4 – figure supplementary 1).

We also generated a antigenic map with the locations of our tested strains shown in the map. We also compared the paired antigenic distance of A(H3N2) strains (including our tested strains). These results (Figure 1 – figure supplementary 3) suggested that the tested strains that we used spanned the circulation of A(H3N2) since its emergence and well covered the antigenic space of the virus.

Reviewer #1 (Public Review):

The authors suggest that there is a long-term periodicity of individual antibody response to influenza A (H3N2). The interesting periodicity may be surely appeared. Though the authors assume that the periodicity is driven by pre-existing antibody responses, the authors could provide more supportive data and discuss some possibilities.

Thank you for your comments and please find our point-to-point responses below.

1) The authors can investigate whether the periodicity reflects an epidemic/invasion record of A(H2N3) within Guangzhou or the surrounding city, e.g., the numbers of flu-infected people yearly can be referred to.

Thank you for your comments. We aimed to investigate the periodicity in individual level antibody responses, so we made several efforts to minimize the impacts of population level A(H3N2) activity in our analyses. In particular, we have removed the average activity at population level (i.e., strain-specific intercepts), to minimize the impact of higher circulation of a certain stain on the periodicity.

In our simulations, we tested models that only incorporated population level activity but not including cross-reactions (Figure 3B, I), which did not recover the observed periodicity. In the models that including both population level activity and cross-reactions, we found that less predictable population level activities (i.e., less regular annual epidemics) would increase the variations in individual-level long-term periodicity (Figure 3G-H). We also found that measured periodicities did not vary substantially when comparing those measured at baseline compared to those measured at follow up (~3-4 years later). These results suggested that the local epidemics may only have limited impacts on the observed periodicity in individual’s antibody responses, while the cross-reactions between previous exposed and currently circulating strains may be the main drivers.

To address this comment, we added a paragraph in discussion (lines 336-342):

“In this study, we did not explore the interactions between individual level antibody responses with population level A(H3N2) activity (e.g., epidemic sizes). We minimized the impacts from population level by performing the Fourier analysis with individual departures from population average and validating the results with data from the Vietnam cohort. Simulation results further suggested that the population level virus activity alone was not able to recover the observed periodicity, though epidemics with less regularity seemed to increase the variability in individual-level periodicity in the presence of broad cross-reactions (Figure 3G-H).”

2) The authors can consider whether the participants are recently/previously vaccinated and/or infected with flu. The remaining antibodies may reflect a long memory but may show a recent activation.

Thank you for your comments. We agree with the reviewer that the observed seroconversion of the circulating strains may reflect responses recent re-exposures. Given the low influenza vaccine coverage in our cohort (1.3%, 10 out of 777) and in China in general (<5% [3, 4]), we believe that our observed periodicity and seroconversion patterns were unlikely to be caused by to recent influenza vaccinations.

We think that the pervasive exposure to A(H3N2) could be a driver to the observed seroconversions to circulating strains between our baseline and follow-up were likely due to the pervasive exposures (or reinfections for those who developed into infections). Using the same data set, we previously reported 98% and 74% of participants experienced 2- and 4-fold rise to any of the 21 tested A(H3N2) strains [5].

As the reviewer and previous studies suggested, the antibody responses could reflect long term memories that were activated after recent exposures [1, 6]. We generated our hypothesis based on this features, and to characterize the periodicity that may arose from the interactions between long term memories and newly generated antibodies.

We incorporate the re-infection mechanism in our simulations, with and without subsequent cross-reactions with previously exposed distant strains (Figure 3I). Results indicate that reinfection alone cannot recover the observed long-term periodicity (Figure 3A), while reinfection plus the resulting cross-reactions can recover such long-term periodicity (Figure 3D). Therefore, we believe that the repeated exposures or re-infections would not affect our reported periodicity, while they may be drivers of continuous formulation of the life-course antibody profiles and the observed periodicity. Of particular note is the consistency of measured periodic behaviour at baseline and follow up (~3-4 years later).

To address this comment, we reported the vaccination status of our participants when introducing the data (lines 127-129) and in the discussions (lines 280-282 and 313-315):

“Only 0.6% (n = 5) of participants self-reported influenza vaccinations between the two visits, therefore, the observed changes in HI titers between the two visits were likely due to natural exposures.”

“Due to the low influenza coverage in our participants and in China in general, the observed seroconversions likely reflected antibody responses after natural exposures during the study period.”

“Particularly, our simulation results suggested that model including repeated exposures or population level A(H3N2) activity alone did not recover the long-term periodicity (Figure 3).”

3) The strains inducing high HI titers may have similar mutations and may be reactive to the same antibodies. What are the mutation frequencies among 21 A(H3N2) strains?

Thank you for your comments. We selected the 21 tested strains to cover the span of the circulation of A(H3N2) strains since 1968 and antigenic diversity. We prioritized with the strains that were included in the vaccine formulation and tested to create the antigenic map by Fonville et al. [1].

We reproduced the antigenic map (up to strains isolated in 2010) by Fonville et al. [1] and compared the antigenic locations of our tested A(H3N2) strains (Figure 1—figure supplement 3). The 21 strains (or their belonging antigenic clusters if the strains were not used for the map) largely tracked the antigenic evolution of A(H3N2) since its emergence in 1968, with a reportedly mutation rate of 0.778-unit changes in antigenic space per year [1, 2].

We further calculated the paired antigenic distance of strains tested in the antigenic map, which was highly correlated with the time intervals between the isolation of the two strains. The figure also suggested our tested strains cover the time spans and antigenic distances that were shown in the original antigenic map. In addition, our observed periodicity was identified in individual time series of residuals, which has removed the shared virus responses or assay measurements (Figure 1). Therefore, we believe that the impact of specific mutations may have limited impacts on our findings.

To address this comment, we included the reproduced antigenic map showing the locations of the tested strains and their pair-wise antigenic distance in Figure 1—figure supplement 3 and referenced in the main text (line 127).

Reviewer #2 (Public Review):

This is a well-thought-out, clearly exposed article. It builds upon the platform of 'original antigenic sin' (OAS), a notion first developed from studying individuals infected with influenza. According to OAS, the initial infection will set the dominant immune response targets (antigens) that immune cells will recognize, such that infection with a related strain will cause a strong response focused mainly against the initially infecting strain, that then goes on to protect against the new-infecting strain. This study builds off this idea, showing that as strains become increasingly antigenically distant as inferred by the time between strain appearance, the cross-protection can drop to a point where it needs to be invigorated with a potentially new response. The potential biological mechanisms behind this aren't discussed, but a model is built that conveys the potential for 'relative risk' of an individual over the course of the life, based essentially on when one was born.

Thank you for your comments. We expanded our introduction hoping to include more biological mechanisms, especially those related with original antigenic sin.

“Antibodies mounted against a specific influenza virus decay (in either absolute magnitude or antigenic relevance) after exposure until re-exposure or infection to an antigenically similar virus occurs, whereupon back-boosting of antibodies acquired from previous infections (e.g., activation of memory B cells) can occur, as well as updating antigen specific antibodies to the newly encountered infection (e.g., activation of naïve B cells.” (lines 80-84)

“Original antigenic sin (OAS) is a widely accepted concept describing the hierarchical and persistent memory of antibodies from the primary exposure to a pathogen in childhood. Recent studies suggested that non-neutralizing antibodies acquired from previous exposures can be boosted and may blunt the immune responses to new influenza infections.” (lines 92-97)

The basic premise was to measure from serum influenza haemagglutinin-inhibition (HI) titers of 21 strains of influenza A (H3N2) - related strains causing disease at various times over a period of some 40 years- from a diverse set of ≈800 participants of various ages, at two time points, spaced 2 yr apart. The authors then calculated the HI titer for the 21 strains for each individual. From this, each participant's age, their age at the time of a strain's development, and when a strain emerged were used to assess whether there was periodicity to immune responses by performing a splined Fourier transform for each individual and then examining the composite pattern across time for HI titers. The authors propose that on average there is a 24-year periodicity to immune responses to influenza strains, such that after the initial infection, cross-reactivity reduces to the point where it may be less meaningful for protection over around 24-year, and suggests activation of a 'new' immune response might be required to control the more distant strain involved in the response at that time. The periodicity was longer than would be predicted if age were not a factor involved in the HI titer patterns across time. Further, variability in the periodicity was shown to involve broad cross-reactivity between strains and narrow cross-reactivity in more highly-related (closer in time) strains, individual HI titer, and periodic population fluctuations. In the literature, viral strains are estimated to mutate to the point of losing 50% cross-reactivity with a T1/2 of approximately 2.5 yr, which would make the inferred lifespan plausible but perhaps surprisingly long, implying there are immune feedback parameters that influence periodicity. The authors also use an independent cohort of approximately 150 individuals from a separate, published, study to validate some findings revealed in the primary data set.

Thank you for your comments and sorry for the confusion. We agree with the reviewer that the onward protection from the cross-protection should be shorter than 24-year periodicity that was identified in the retrospective antibody responses. We hope to clarify that we identified long-term periodicity by retrospectively investigating the individual antibody profiles, which were results of multiple previous exposures and immunity and cross-reactions that arose from these previous exposures. Therefore, the long-term periodicity is a retrospective characterization, and should not be directly interpretated as the duration of onward protection.

As shown in Figure 4A, the 24-year periodicity consists of phases when individuals’ titers are higher (phase I & II) and lower (phase III & IV) than the population average. As such, the duration of onward protection may be shorter than the entire periodicity. Assuming the protection decreasing with lower titer levels, the onward protection is expected to decrease in phase II and take 1-6 years to drop from the furthest to population average. This is consistent with findings that homotypic cross-protection against PCR-confirmed infections up to about five seasons (lines 291-293), but whether such protection is driven by the declining of cross-reactions still need further investigations.

To address this comment, we rephrased our discussion and make the interpretation less confusing. (lines 285-287):

“Of note, the long-term periodicity is a retrospective characterization of individual antibody profiles that arose from multiple exposures and cross-protection, which should not be directly interpreted as the duration of onward protection conferred by the existing antibodies.”

Strengths: Overall, the study is well executed and the patterns that are visually apparent in Figure 1A (the 'raw' data) are built on to inform a model of the potential breadth of cross-reactivity in a given individual at any given time after birth, integrated with the influenza strains to which they are most likely to have been first exposed. It is a complex thing to make sense of data involving many individuals who could be infected or vaccinated at any and variable points in time over the course of their life, but the authors derive a model that probabilistically accounts for possible infection events, so controls for this nicely, or at least to a degree that is practicable.

Thank you for your supportive comments. We hope to clarify that we identified the long-term periodicity using the residuals of individual HI titers after extracting the population activity that is visually noticeable in Figure 1A. By doing this, we hope to minimize the impacts of population level A(H3N2) activity and laboratory measurements on individual antibody responses (Figure 1C; detailed methods in lines 396-412).

Questions related to the main limitation: The level of math in this paper makes it hard for a basic biologist to critique the approach, but the argued points are intriguing. Foremost, in the final part of the paper the authors move from building a model to testing its potential to predict HI titers in the final quarter strains of the study period, placing individuals into one of four phases: I) early increasing to high titer response, II) waning response phase where they are returning back to the average population-level response against a strain, III) sub-par response against a strain and then reinitiation of HI titers in phase IV. Pleasingly this shows a good correlation between individuals' ages and their predicted phase. However, while the fit predicts phase well in Fig 4C and 4D, it looks to perform less adequately in Fig 4B.

1) Why is this?

Thank you for your comments and sorry for the confusion. In Figure 4B, we aimed to characterize and predict the position instead of the amplitude in the individual time series of residuals. Therefore, we fitted the model using only harmonic terms (i.e., sine and cosine functions; Equation 12 on page 26) [7], while we believe there may be other factors that could affect the observations but were not included in the model. The perditions from the model inform the position and velocity of harmonic oscillators rather than the amplitude or extent of the wave, therefore, the predictions did not exactly fit the observations.

To address this comment, we expand the corresponding methods hoping to make it clear (lines 661-663):

“Of note, we fitted the model aiming to estimate the position of the harmonic oscillators and did not consider for other non- harmonic factors, therefore the model may not fully capture the variations of the data.”

2) Another point for consideration is that the time between samplings (2010-2012) is comparatively short, given a 24-yr predicted periodicity. What would happen to the predictions if the periodicity were 35-yr or 6-yr? Would the model fail to call individuals accurately in these cases?

Thank you for your comments. We repeated our predictions in Figure 4F-G by assuming a 35-year and 6-year periodicity respectively as suggested. Results suggested that model predictions with either 35-year or 6-year did not outcompete the model predictions assuming a 24 years old (Figure 4—figure supplement 1). For instance, the observed proportion of seroconversion to circulating strains in each cohort have correlation coefficients of 0.49 (p-value = 0.05), 0.63 (p-value = 0.02) and -0.12 (p-value = 0.69) with the predicted proportion of phase IV when assuming a 35-, 24- and 6-year periodicity, respectively.

We also hope to clarify that we investigated the prediction potentials of long-term periodicity from two perspectives. Except for using the periodicity to predict the seroconversions between baseline and follow-up, we also predict the phase of each individual in the year of 2012 only using HI titers against strains that were isolated before 2002. Our results suggested our 10-years ahead predictions well correlated with observations (Figure 4C).

To address this comment, we also included the results of analyses using alternative 35- and 6-year periodicity as Figure 4—figure supplement 1, and reported in the main text (lines 262-264).

3) Similarly, if the samples were taken further apart, would the model still be effective at predicting phase?

Thank you for your comments. We hope to clarify that we collected two cross-sectional serum samples, while we identified the long-term periodicity and predicted phase with serums collected from each visit, separately. For instance, in our sensitivity analysis that using serum collected in follow-up (Figure 1—figure supplement 1), we revealed similar long-term periodicity (baseline in Figure 1) with that identified using the baseline serums, despite pervasive exposures during this time period (time separating samples varied from 3-4 years). In addition, the Vietnam data collected sera from six consecutive years. These data showed a similar long-term periodicity (Figure 2—figure supplement 5).

For the phase prediction, we used residuals of HI titers against 14 historical strains that were isolated between 1968 and 2002, and predicted the phase of strain that was isolated in the year 2012. This prediction was derived purely by depending on the periodic pattern of the time series and without information for strains isolated 10 years prior to 2012. Therefore, the prediction was 10 years ahead and was well correlated with observations from the complete time series, further supporting that there may be an intrinsic cycling in individual antibody responses and that this cycle is fairly stationary and predictable.

Author Response

Reviewer #1 (Public Review):

While the circuits underlying the computation of directional motion information in the fly brain are very well described, much less is known about the neurons serving the detection of objects. In a previous publication from the same lab, it has been shown that flies perform body saccades to track a moving object during flight. In the current paper, Frighetto and Frye provide evidence that T3 cells, a population of neurons within the optic lobes, are involved in this task. First, they performed 2-photon Calcium imaging from T3 cells to show that these cells respond to moving bars, which they later use in behavioural experiments. They then silenced T3 cells using genetic tools and tested the behavior of these flies in response to a rotating bar using two different setups. In one, the flies are fixed and bilateral changes in wing stroke amplitude are used as a measure for turning, in the other, flies are magnetically tethered such that they can rotate around the vertical body axis. Silencing T3 cells leads to the abolishment of the steering response induced by object position using a bar that is defined by its motion relative to the surround, but leaves the response to object motion intact. In the magnetically tethered flies, it reduces the number of saccades and thus leads to an impairment of bar-tracking behavior. In another set of experiments they optogenetically activated the whole population of T3 neurons (which supposedly impairs their normal function), which leads to an increase in the number of saccades after the activation (when the light stimulus used to activate the cells is turned off). Silencing the neurons necessary for detection of local motion, T4 and T5 cells, in contrast reduces responses elicited by object motion rather than position, but also has an impact on object tracking saccades. The authors provide a simple model, where speed-dependent signals from multiple T3 cells are integrated and trigger a saccade, when a threshold is reached.

The data generally support the conclusion that T3 cells play a role in detecting bar position and in controlling saccades in response to rotating bars. However, there are some inconsistencies in the data that are not sufficiently explored and discussed.

1) In a previous paper from the lab (Keleş et al., 2020), it was shown that T3 cells respond preferentially to small objects, whereas here they robustly respond to elongated bars and even large-field gratings. This discrepancy is not discussed.

The most likely explanation is that Keleş et al. (2020) work used stimuli of half-contrast (or lower) to probe contrast polarity effects, whereas our stimuli here match the behavior experiments using maximum contrast broadband stimuli. Keleş et al. (2020) work also provided visual stimuli over the full display, >200-degrees in azimuth, whereas here we only provide stimuli unilaterally over <100 degrees; perhaps there was some effect of contralateral stimulation. Finally, different Gal4 drivers; here we use a split-Gal4 that is highly specific for T3. Keleş et al. (2020) work used a normal Gal4 driver less clean than the split. We shall discuss these discrepancies in revision.

2) In a previous paper, the authors showed that integrated positional error rather than bar position is used to elicit bar-tracking saccades and that saccade amplitude is relatively stereotyped. However, here they show, that T3 cells respond much more strongly to a slowly moving stimulus (18{degree sign}/s) rather than to the fast moving stimuli used for the behavioral experiments (> 90{degree sign}/s). This response property plays an important role for the model they propose. My general concern here is that the findings might not be generalizable to slower moving bars, where more precise, position-dependent responses could play a larger role, and that these fast moving bar stimuli represent an extreme situation, where the flies cannot accurately track bar position any more.

We agree that flies will not accurately track purely positional cues at higher bar speeds, since responses to positional signals are inherently sluggish. In free-flight, files execute orientation saccades when a stationary post subtends ~30 degrees (bar width used here), at which point the leading edge of the post is moving ~250°/s (van Breugel and Dickinson 2012). Thus, higher bar speeds are the norm for flies, and our behavioral stimuli (90°/s) was chosen to robustly trigger tracking saccades and to compare with previously published behavioral data sets. Bar velocity of 18°/s is far below the range that robustly triggers orientation saccades. We image at 90°/s and 180°/s to show that T3 responses to behaviorally relevant bar speeds could reasonably act as inputs to an integrate-and-fire behavioral controller. These points shall be clarified in revision.

3) The claim that T3 cells are tuned to stimulus velocity is not supported by the data in my view. For the bar stimuli, the authors only tested speeds of 18{degree sign}/s and above 90{degree sign}/s, but nothing in between. For the grating motion there seems to be an influence of temporal frequency for the same stimulus velocity (see e.g. Fig.1_1), but this is not quantified.

We shall add a full spatiotemporal response profile in revision. One note: we presented T3 responses to different grating speeds in Supplemental material because our goal was merely to indicate speed sensitivity by T3, rather than to present a comprehensive speed tuning curve. T3 is distinct from T4 and T5 in that it is not directionally selective, is full-wave rectified for contrast, and shows similar responses to bars of differing temporal frequencies moving at the same speed. These properties are also likely accompanied by a broad spatial frequency sensitivity (which would bestow speed tuning), but in revision shall either demonstrate this or remove claim to it.

4) The results from the optogenetic activation experiments are hard to interpret, as it is unclear how a prolonged activation of all T3 cells would affect the downstream circuitry. It is not clear that this experiment is equivalent to a "loss-of-function perturbation" of T3 cells as the authors claim in the text.

We are making an assumption, which we shall clarify in revision, that downstream circuitry requires a spatiotemporal progression of columnar activity, as would be generated by the projection of a discrete bar-type-object moving across the eye, and that activation of all columnar inputs together, as would occur with CsChrimson stimulation, would disrupt this discrimination. Although it is a supposition, we feel that it is parsimonious. We compared the effect of CsChrimson stimulation under two different LED intensities but found no effect on bar tracking behavior.

Reviewer #2 (Public Review):

In their manuscript titled "Feature detecting columnar neurons mediate object tracking saccades in Drosophila", Frighetto & Frye study the effect manipulating T3 neurons has on tethered flight saccades. The authors first characterize the responses of T3 neurons to simple visual stimuli, and then manipulate T3 cells (with both Kir2.1 and CsCrimson) and study the effects on the fly's tethered flight behavior, focusing on different types of sharp turns (saccades). Finally, the authors suggest an integrate and fire model to explain how an array of T3-like neurons can produce some of the recorded behavior.

The authors study the elementary, yet challenging, computation of object discrimination. They hone in on a cell type that most likely plays an important role in the circuit. However, the authors do not sufficiently clarify the framework in which they conceptualize T3's role in object discrimination, neither when discussing it in the introduction/discussion nor when explaining experimental results. The authors present the work in comparison to T4/T5 cells. However, T4/T5 cells have been shown to be both local motion detectors and the main cell types to compute motion in the fly's eye. Downstream neurons integrate over these local units to detect different patterns of global and local motion (Authors should cite Krapp 1996 Nature). Are the authors suggesting that T3 neurons perform a similar function only as local object detectors? That is a bold claim that will need to be supported with more experimental results and reconciled with previous results. We already know of other Lobula Columnar neurons (LCs) that respond to different sizes, some even smaller than the optimal T3 stimulus (e.g. Klapoetke 2022 Neuron) and we know of LCs that respond to small objects that do not receive major inputs from T3 cells (e.g. Hindmarsh 2021 Nature).

We are attempting to posit a simple and parsimonious framework for T3 action. Are T3 neurons “local object detectors”? T3 is clearly not “selective” for local objects, since we show that they respond to elongated bars and wide-field gratings (at least when projected over the ipsilateral visual hemisphere). T3 is, however, “sensitive” to objects: vertical bars yielded a mean response peak ~1 ΔF/F whereas a small square object elicited a peak of ~4 ΔF/F (Keleş et al., 2020). This amplitude differential likely indicates surround inhibition, but does not preclude a downstream integrating neuron from pooling columnar inputs to assemble a spatial receptive field for either an elongated bar or a small object. Individual T4/T5 neurons show roughly double the response amplitude to a small object than a long vertical bar (Keleş et al., 2020), which is consistent with other reports, but one would not classify T4/T5 as “small object detectors” as they play a fundamental role in detecting wide-field motion stimuli. We intend to posit that (i) columnar T3 neurons are small-field (local) detectors of the features contained within stimuli that flies readily track, (ii) that the integration of these local signals could support the integrated error computations that flies make to track bars, which (iii) explains why T3 blockade compromises bar tracking saccades. We do not mean to claim that T3 are the first, last, or only inputs to object detection circuitry in deeper neuropiles. We shall endeavor to clarify these issues in revision.

These differences between T4/T5 cells and T3s also make interpreting the experimental manipulations more challenging. When hyperpolarizing T4/T5 or 'blinding' them with CsCrimson activation, the visual motion circuit is severely disrupted. However, the same cannot be said about inactivating/blinding T3 neurons and the object detection circuit (if it is indeed a single circuit). The authors are justified in deducing a connection between blocking T3 neurons and a reduction in bar tracking, but generalizing the results to object detection requires more experiments and clarifications.

We consider “bar tracking” to be one form of object detection, but not the only form. A bar is an “object” (albeit a tall object) in the sense that it is optically disparate from the visual surround. Thus, inactivating/blinding T3 indeed severely disrupts the detection of bar-type-objects. We shall clarify the language to remove any confusion between “object” and “bar”. We do not mean to generalize T3 function to all object vision in the same way that T4/T5 function is generalized to all motion vision, and this shall be clarified in revision.

When framing the manuscript in the object detection framework, previous results regarding the definition of an object should also be addressed. Maimon Curr. Biol. 2008 and work from their own lab (Mongeau, 2019) have already shown that tethered flies respond differently to bars and small objects (fixating on the former while anti-fixating on the latter). Previous work has also shown that T3 neurons respond strongly to small objects and suppress responses to long bars (Tanaka Curr. Biol. 2020). Since all the behavioral experiments in the current manuscript and all the visual stimuli are full arena-length bars, it is impossible to tell whether the T3 results generalize to small objects and even how to reconcile the stronger response to small objects with the role ascribed to T3 cells in generating behavioral responses to long bars.

This amplitude differential between small object and elongated bar responses by T3 likely indicates surround inhibition, but does not preclude a downstream integrating neuron from pooling columnar inputs to assemble a spatial receptive field for either an elongated bar or a small object. Consider that T4/T5 neurons show roughly double the response amplitude to a small object than a long vertical bar (Keleş et al., 2020 and consistent with other reports), but one would not classify T4/T5 as “object detectors” as their small-field columnar signals are integrated by downstream wide-field neurons that assemble spatial filters for specific patterns of optic flow that are generated during flight maneuvers (Krapp et al., 1996 Nature). One downstream integrator of T3 inputs, LC11, is more selective for small objects than T3. We shall clarify these points in revision.

Finally, the authors propose a model for a hypothetical neuron downstream of T3 that would integrate over several T3s and generate saccades. However, given the current knowledge level in the fly vision field, the model should either be grounded more in actual circuit connectivity or produce testable predictions that would guide further research.

We are currently working on the putative downstream partners of T3, and testing for the integration of T3 signals. Preliminary data show that silencing a specific LC class postsynaptic to T3 recapitulates the effects of silencing T3 on saccadic bar pursuit. In the revised version of the manuscript we will provide additional discussion.

The authors should decide whether they would like to address these concerns with more specific experiments that would shed light on the role T3 has to play under different conditions and different definitions of a visual object, or whether they would prefer to limit the scope of their claims.

We shall endeavor to do both!

Reviewer #3 (Public Review):

In free flight, flies largely change their course direction through rapid body turns termed saccades. Given how important these turns are in determining their overall behavior and navigation, it is important to understand the neural circuits that drive the timing of triggering these saccades, as well as their amplitude. In this paper the authors leverage the powerful genetic tools available in the fruit fly, Drosophila, to address this question by performing physiology experiments as well as behavioral experiments with inactivation and activation perturbations.

The authors make three primary conclusions based on their experiments: (1) the feature detecting visual pathway (T3) is responsible for triggering saccades in response to moving objects, but not widefield motion, (2) the pathway primarily responsible for wide field motion encoding (T4/T5) is responsible for triggering saccades in response to widefield motion, and (3) the T4/T5 pathways is responsible for controlling the amplitude of both object and widefield motion triggered saccades.

The authors go on to show that using calcium imaging data of T3 activity it is possible to predict under what conditions flies will initiate a saccade when presented with objects moving at different speeds, resulting in a parsimonious model for how saccades are triggered.

Together, the imaging, behavior, and modeling provide compelling evidence for claims 1 and 2, however, the evidence and modeling for point 3 - the amplitude of the saccades - is lacking. The statistical analysis does not go into sufficient detail in comparing across different cases, and in particular, there is little mention of the effect sizes, which appear to be quite small (this is primarily in reference to 3F and 4E). The data suggest that both the T3 and T4/T5 pathways contribute to saccade amplitude, instead of T4/T5 being the only or primary drivers.

We agree that the evidence suggests that both T3 and T4/T5 pathways contribute to saccade amplitude for bar tracking behavior, and shall clarify this conclusion in revision. However, we also note that the effect of silencing T4/T5 is more prominent (e.g., peak angular velocity) and more consistent across visual conditions. We will dig deeper into the data to substantiate this point. The effect sizes might be small because the silencing approach (i.e., inward rectifying Kir2.1 channels) maintains a hyperpolarized state but does not completely block neuron function; consider that the wide-field optomotor responses of T4/T5>Kir2.1 flies is reduced but not eradicated (Fig. 3A_1).

Author Response

Reviewer #1 (Public Review):

Li et al. have designed a study that examines specific mechanisms for how different DNA sequence variants in the common cancer gene p53 (also known as TP53) influence the sensitivity of tumors to a variety of common cancer treatments. Specifically, they examine a handful of p53 variants with respect to glioblastoma and its response to platinum-based chemotherapy and to radiation therapy. The authors begin by mentioning that looking at DNA variants in cancer is useful but also incomplete: methylation, PTMs, and non-DNA sequence variants can also be critical. They then mention that they have created a model showing that nearly all cancers with p53 mutations have loss-of-function variants and that many cancers with "normal" wildtype p53 in fact have variants causing LOF. These p53 LOF tumors lead to worse patient outcomes, but the authors here show that these tumors appear to be more susceptible to radiation and platinum-based chemotherapy, which they say they have validated in glioblastoma xenografts. This potentially opens up a new avenue for precision medicine for many different sources of cancer that share common p53 LOF variants. The authors have taken a modern approach towards cancer diagnosis and shown how this can improve targeted treatments across a large array of cancer types. They have provided a reasonably convincing proof of concept of this approach for n = 35 PDXs in one cancer type. By and large, the approach and results are reasonable, although many of the exact results concerning the genes and pathways identified that covary with the various treatments and p53 variants are unclear. For instance, the feature selection seems to be somewhat ad hoc, e.g. the method used to determine p53 LOF from p53 WT in the TCGA data was not the same method used for determining p53 LOF from p53 WT in the PDX data.

Thanks for the positive comments. In our study, we used the same method for feature selection (i.e., p53 targets identification), and for calculating CES in different cancer types. This is described in Materials and Methods. However, the methods used to identify the LOF of WT TP53 in TCGA and PDX data are different. For TCGA LUNG, BRCA, COAD, ESCA cohorts, we used the SVM models built from the same cancer type to predict TP53 status. For PDX samples derived from the glioblastoma patients, we used the unsupervised clustering approach. This is because:

1) To train an SVM model, we need a large number of “normal” samples (to represent p53 normal status) and “tumor samples with TP53 truncating mutation” (to present p53 LOF status). In this PDX cohort (n = 35), we have no “normal” samples and only one p53-truncating mutation (Fig. 4f, Table S6). Technically, it is impossible to build an SVM model from this PDX cohort.

2) The TCGA GBM cohort also has very limited “normal” samples (n = 5) which prevents us from training an SVM model for glioblastoma prediction.

3) The TCGA pan-cancer SVM model is not a good choice since GBM was not included into the pan-cancer cohort due to its limited training sample size. Although the pan-cancer model achieved a high AUROC, its performances varied significantly across cancer types. This is most likely due to the imbalanced sample size, since the pan-cancer model is biased by cancer types (e.g., lung and breast) with the larger sample sizes.

4) Even we were able to build a new SVM model from the TCGA pan-cancer with GBM samples included, applying this SVM model to predict non-TCGA samples is still very challenging because of batch effects.

Therefore, we first used the unsupervised clustering as an alternative to the SVM model to classify samples, and then we manually annotate the PDX clusters into “p53-pN” and “p53-pLOF” according to the composite expression score.

We agree with the reviewer that the underlying pathways/mechanisms that can potentially explain the different treatment effects and p53 non-mutational LoF are still unclear and warrant further investigation.

The TCGA AUROCs were incredibly good - over 99% - versus more like 75% for the actual proof of concept. While any significant p-value is fine for basic research, it would be nice to know how this could be improved and bring the results in Figure 4 from ~75% to the >99% that would be necessary for use as a medical diagnostic or for treatment selection for precision medicine.

Thanks for your suggestion. Precision cancer medicines that target TP53 mutations are currently being evaluated in clinical trials. Developing a robust model to predict p53 functional status for medical diagnosis or treatment selection is the primary goal of our study. However, there is still a long way to go to bring the model trained from external data into medical practice. To minimize the biological, clinical and technological heterogeneities and bias, the best approach is to train an SVM model from the same cancer type in the same institute; this requires:

1) The sample sizes of both normal and tumors harboring TP53 truncating mutation should be sufficient to train the SVM model. Take the TCGA lung cancer dataset (n_tumor = 1003) as an example, we built an excellent SVM model from 108 normal samples and 254 tumor samples with TP53 truncating mutations. A much larger sample size is needed if the TP53 truncating mutation frequency is low.

2) Matched data including whole-exome or whole-genome sequencing (to determine TP53 mutation status), RNA-seq (for gene expression), and treatment response.

If one plans to use public data such as TCGA to train the model, the major challenge is integrating data from different sources (i.e., remove batch effects arising from different patients’ cohorts, tumor samples storage and processing, library preparation, sequencing, and bioinformatics analyses).

However, there are significant questions regarding the specific findings uncovered: do the gene pathways identified through bioinformatic analysis fit in with the many highly-studied mechanistic roles of p53? Do the cohort selections - which vary by an order of magnitude in sample size, and come from different locations and different tissues - make statistical sense for cross-validation?

According to our analysis, p53 targets shared by four selected cancer types are significantly enriched in “cell cycle control” and “DNA damage response” pathways, which are the canonical functions of p53 (PMID: 9039259, PMID: 36183376).

For the four TCGA cancer cohorts selected in our study, cross-validations were independently performed for each cancer type. For the pan-cancer cohort, we agree with the reviewer that the samples come from different locations and different tissues, and the pan-cancer SVM model could be potentially biased by a few cancer types with larger number of samples. Building a pan-caner SMV model is a compromised strategy when each cancer type alone does not have sufficient samples to train its own SVM model, and more rigorous evaluations (by independent datasets) are needed. This is why we put the pan-cancer results into the supplementary materials. We have revised the manuscript to make this point clear (Page 9).

Author Response

Reviewer #1 (Public Review)

[...] One potential issue is that the high myelination signal is associated with the compartment in V2 (pale stripes) which was not functionally defined itself but by the absence of specific functional activations. No difference was reported between those stripes that were defined functionally. Other explanations for the differential pattern of a qMRI signals, e.g. ROI distribution for presumed pale stripes is not evenly distributed (more foveal), ROIs with low activations due to some other factor show higher myelin-related signals, cannot be excluded based on the analysis presented.

Indeed, it would have been advantageous to directly functionally delineate pale stripes in V2. Since we were not able to achieve this by fMRI, we needed an indirect method to infer pale stripe contributions in the analysis. We also added a statement in the discussion section to emphasize this more (p. 9, lines 286–288).

Furthermore, different myelination between thin and thick stripes was not tested, since we did not have a concrete hypothesis on this. Despite the conflicting findings of stronger myelination in dark or pale CO stripes in the literature, no histological study stated myelination differences between dark CO thin and thick stripes. Therefore, our primary interest and hypothesis was lying in comparing the different myelination of thin/thick and pale stripes using MRI.

Thank you very much for this comment about potential other sources of differential qMRI parameter patterns. Indeed, based on the original analysis we could not exclude that the absence of functional activation around the foveal representation may have biased our analysis. We therefore added a supporting analysis, in which we excluded the region around the foveal representation from the analysis. The excluded cortical region was kept consistent between participants by excluding the same eccentricity range in all maps. We added more details in the results section of the revised manuscript (p. 8, lines 189–202). In Figure 5-Supplement 1 and Figure 5-Supplement 3, results from this supporting analysis are shown which reproduced the primary findings from the main analysis, particularly the relatively higher myelination of pale stripes.

ROI definitions solely based on fMRI activation amplitude have additional limitations. However, we find it unlikely that a small fMRI effect size and low contrast-to-noise ratio (i.e. stochastic cause of low statistical parameter values/”activation”) has impacted the results, since Figure 3 shows that we could achieve a high degree of reproducibility for each participant.

We would note that the fact that we found consistent differences across MPM and MP2RAGE sessions makes some potential artifacts driving the differences unlikely. We also find it unlikely that systematic cerebral blood volume differences between stripes would have driven the results. A higher local blood volume would lead to increased BOLD responses but also to a higher R1 value due to the deoxy-hemoglobin induced relaxation, which is opposite to the observation of higher activity in the thick/thin stripes but lower R1 values.

Further studies using other functional metrics (e.g. VASO, ASL etc.) may help us to even more clearly demonstrate specificity but were out of the scope of this already rather extensive study. Although we have added extensive further analyses in the revised manuscript such as controlling for foveal effects or registration performance, we did not see a possibility to fully exclude a systematic bias that might potentially be caused by unknown factors.

Another theoretical and practical issue is the question of "ground truth" for the non-invasive qMRI measures, as the authors - as their starting point - roundly dismiss direct histological tissue studies as conflicting, rather than take a critical look at the merit of the conflicting study results and provide a best hypothesis. If so, they need to explain better how they calibrate their non-invasive MR measurements of myelin.

We agree and have now further elaborated on the limits of specificity of the R1 and R2* signal as cortical myelin marker (p. 2, lines 68–88; p. 6, line 163; p. 8, line 216; p. 9, lines. 257–260). However, we still think that it is important for the reader to appreciate the conflicting results in histological studies using staining methods for myelin, which adds to the study’s background.

We did not intend to give the impression that MRI provides the missing ground-truth to adjudicate histological controversies, but that it provides an alternative and additional view on the open questions. We changed the introduction to better reflect the aspect that the study offers a unique view by providing myelination proxies and functional measures in the same individual, which allows for direct comparison and investigation of structure-function relationships (see p. 2, lines 68–70; p. 3, lines 93–95), which is not accessible to any other approach. Nevertheless, we would like to note that R1 has been well established as a myelin marker under particular conditions (Kirilina et al., 2020; Mancini et al., 2020; Lazari and Lipp, 2021). It has also been widely used for cortical myelin mapping across a variety of populations, systems and field strengths. We added this statement to the introduction (see p. 2, lines 82-85). We note that we excluded volunteers with pathologies or neurological disorders from the study and their mean age was about 28 years. Thus, we had conditions comparable to previous (validation) studies.

Because of the contradictory findings of histological studies, we could not further finesse the hypothesis beyond our previous a priori hypothesis that we expected differences in the myelin sensitive MRI metrics between the thin/thick versus pale stripes. To improve the contextual understanding, we added a paragraph in the discussion section covering in more depth how the MRI results relate to known histological findings (see pp. 8–9, lines 216–240).

While this paper makes an important contribution to the question of the association of specific myelination patterns defining the columnar architecture in V2, it is not entirely clear whether the authors can fully resolve it with the data presented.

Indeed, we agree that non invasive aggregate measures, such as the R1 metrics, offer limited specificity which precludes a fully conclusive inference about cortical myelination. We have further emphasized this on several occasions in the text (see p. 2, lines 68–88; p. 6, line 163; p. 8, line 216; p. 9, lines. 257–260). Since the correspondence of cortical myelin levels and R1 (and other metrics) is an active area of research, we expect that the understanding, sensitivity and specificity of R1 to cortical myelination will further improve. We note that the use of qMRI is a substantial advance over weighted MRI typically used, which suffers from lack of specificity due to instrumental idiosyncrasies and varying measurement conditions.

Reviewer #2 (Public Review)

[...] Unfortunately, this particular study seems to fall into an unhappy middle ground in terms of the conclusions that can be drawn: the relaxometry measures lack the specificity to be considered "ground truth", while the authors claim that the literature lacks consensus regarding the structures that are being studied. The authors propose that their results resolve whether or not stripes differ in their patterns of myelination, but R1 lacks the specificity to do this. While myelin is a primary driver of relaxation times in cortex, relaxometry cannot be considered to be specific to myelin. It is possible that the small observed changes in R1 are driven by myelin, but they could also reflect other tissue constituents, particularly given the small observed effect sizes. If the literature was clear on the pattern of myelination across stripes, this study could confirm that R1 measurements are sensitive to and consistent with this pattern. But the authors present the work as resolving the question of how myelination differs between stripes, which over-reaches what is possible with this method. As it stands, the measured differences in R1 between functionally-defined cortical regions are interesting, but require further validation (e.g., using invasive myelin staining).

We agree that we have inadvertently overstated the specificity of R1 at several occasions in the text. We therefore toned down the statements concerning the correspondence between R1 and myelin throughout the manuscript (e.g. see p. 2, lines 68–88; p. 6, line 163; p. 8, line 216; p. 9, lines. 257–260).

We also removed the phrase that gave the impression that MRI can conclusively resolve the conflicting results found in histological studies. In the Introduction, we changed the corresponding paragraph by emphasizing the alternative view, which can be obtained from MRI by the possibility to investigate structure-function relationships in the living human brain, which would not be possible by invasive myelin staining (see p. 2, lines 68–70; p. 3, lines 93–95).

We acknowledge that – perhaps aside from electron microscopy – all common markers have shortcomings, which limit their specificity. For example, classic histology is not quantitative and resulted in conflicting results. It even includes the very fundamental issue, that the composition of myelin varies across the brain and within brain areas significantly (e.g., its lipid composition (González de San Román et al., 2018)). Thus, we regard the different invasive/non-invasive measures as complementary. R1 adds to this arsenal of measures and can be acquired non invasively. It has been shown to be a reliable myelin marker under certain circumstances. It follows the known myeloarchitecture patterns of the human brain, which was also checked for the data of the present study (see Figure 4 and Appendix 2). It is responsive to traumatic changes (Freund et al., 2019), development (Whitaker et al., 2016; Carey et al., 2018; Natu et al., 2019) and plasticity (Lazari et al., 2022). Since we studied healthy volunteers with no known pathologies that were sampled randomly from the population, we believe that the previous results generally apply and suggest sufficient specificity of the R1 marker. Of course, we cannot fully exclude bias due to unknown factors that have not been investigated/discovered by validation studies yet. However, in this case we expect that the systematic differences between stripe types would remain an important result most likely pointing to another interesting biological difference between stripes.

While more research is needed to clarify the precise role of R1 for cortical myelin, we think that the meaningful determination of quantitative MR parameter within one cortical area is still interesting for the neuroscientific community.

Moreover, the results make clear that R1 differences are not sufficiently strong to provide an independent measure of this structure (e.g., for segmentation of stripe). As such, one would still require fMRI to localise stripes, making it unclear what role R1 measures would play in future studies.

Indeed, the observed small effect sizes in the present study still requires a functional localization with fMRI. We expected small effect sizes using R1 and R2* due to the known small inter-areal or intra-cortical differences of MRI myelin markers. Therefore, this study aimed at a proof-of-concept investigating whether intra-areal R1 differences at the spatial scale of columnar structures can be detected using non-invasive MRI. Our study shows that these differences can be seen but currently not at the single voxel level. We anticipate that with further improvements in sequence development and scanner hardware, high-resolution R1 estimates with sufficient SNR can be acquired making fMRI redundant (for this kind of investigations). Please see the reply to the next comment concerning the impact of using R1 in future studies.

The Introduction concludes with the statement that "Whereas recent studies have explored cortical myelination ... using non-quantitative, weighted MR images... we showed for the first time myelination differences using MRI on a quantitative basis". As written, this sentence implies that others have demonstrated that simpler non-quantitative imaging can achieve the same aims as qMRI. Simply showing that a given method is able to achieve an aim would not be sufficient: the authors should demonstrate that this constitutes an important advance.

Thank you for this comment. It goes to the heart of the concerns raised about specificity and sensitivity of MRI based myelin metrics. We elaborate here on the main advantage of using qMRI in our current study and why it is more specific than weighted MR imaging. However, we emphasize that a thorough comparison between qMRI and weighted MRI is highly complex and refer to our recent review paper on qMRI for further details (Weiskopf et al., 2021), which are beyond the scope of our paper. The signal in weighted MRI, even when optimally optimized to the tissue of interest, additionally depends on both inhomogeneities in the RF transmit and receive (bias) fields. Other methods like using a ratio image (T1w/T2w) can cancel out the receive field bias entirely (in the case of no subject movements between scans) but not the transmit field bias. This hampers the direct analysis and interpretation of signal differences between distant regions of the brain. For high resolution imaging applications, the usage of high magnetic fields such as 7 T is beneficial or even mandatory due to signal-to-noise (SNR) penalties. With increasing field strength, these inhomogeneities also apply to small regions as V2. For these cases, qMRI is advantageous since it provides metrics which are free from these technical biases, significantly improving the specificity. As high-field MRI has the potential to non invasively study the structure and function of the human brain at the spatial scale of cortical layers and cortical columns, we believe that the results of our current study, which successfully demonstrate the applicability of qMRI to robustly detect small differences at the level of columnar systems, is relevant for future studies in the field of neuroscience.

We emphasized these considerations in the revised manuscript (see. p. 9, lines 273–285).

The study includes a very small number of participants (n=4). The advantage of non-invasive in-vivo measurements, despite the fact that they are indirect measures, should be that one can study a reasonable number of subjects. So this low n seems to undermine that point. I rarely suggest additional data collection, but I do feel that a few more subjects would shore up the study's impact.

The present study was conducted in line with a deep phenotyping study approach. That is, we focused on acquiring highly reliable datasets on individuals. We did not intend to capture the population variance, which is often the goal of other group studies, since low level and basic features such as stripes in V2 are expected to be present in all healthy individuals. Thus we traded off and prioritized test-retest measurements for fMRI sessions and using an alternative MP2RAGE acquisition over a larger number of individuals. This resulted in 6–7 scanning sessions on different days for each individual, summing up to 26 long scanning session in total. We also note that the used sample size is not smaller than in other studies with a similar research question. For example, another fMRI study investigating V2 stripes in humans used the same sample size of n=4 (Dumoulin et al., 2017).

The paper overstates what can be concluded in a number of places. For example, the paper suggests that R1 and R2 are highly-specific to myelin in a number of places. For example, on p7 the text reads" "We tested whether different stripe types are differentially myelinated by comparing R1 and R2..." Relaxation times lack the specificity to definitively attribute these changes purely to myelin. Similarly, on p11: "Our study showed that pale stripes which exhibit lower oxidative metabolic activity according to staining with CO are stronger myelinated than surrounding gray matter in V2." This implies that the study directly links CO staining to myelination. In addition to using non-specific estimates of myelination, the study does not actually measure CO.

We agree that we did not clearly point out the limitations of R1 myelin mapping. Therefore, we toned down the statements about the connection between cortical myelin and R1. The mentioned statements in the reviewer’s comment were changed accordingly (see p. 6, line 163; p. 11, lines 353–354). We also included a small paragraph to clarify the used terminology (color-selective thin stripes, disparity-selective thick stripes) in the manuscript (see p. 4, lines 110–114) to avoid the inadvertent conflation of CO staining and actually measured brain activity.

I'm confused by the analysis in Figure 5. I can appreciate why the authors are keen to present a "tripartite" analysis (thick, thin, and pale stripes). But I find the gray curves confusing. As I understand it, the gray curves as generated include both the stripe of interest (red or blue plots) and the pale stripes. Why not just generate a three-way classification? Generating these plots in effect has already required hard classification of thin and thick stripes, so it is odd to create the gray plots, which mix two types of stripes. Alternatively, could you explicitly model the partial volume for a given cortical location (e.g., under the assumption that partial volume of thick and thin strips is indicated by the z-score) for the corresponding functional contrast? One could then estimate the relaxation times as a simple weighted sum of stripe-wise R1 or R2.

Figure on weighted average of stripe-wise R1 and R2. (a) shows the weighted sum of R1 (de-meaned and de-curved) over all V2 voxels. z-scores from color-selective thin stripe experiments and disparity-selective thick stripes were used as weights in the left and middle group of bars, respectively. An intermediate threshold of zmax=1.96 was used, i.e., final weights were defined as weights=(z-1.96). Weights with z<0 were set to 0. For pale stripes (right group of bars), we used the maximum z-score value from thin and thick stripe measurements. We then set all weights with z≥1.96 to 0 and used the inverse as final weights. i.e., weights = -1 * (max(z)-1.96). (b) shows the same analysis for R2. Error bars indicate 1 standard error of the mean.

(1) Yes, indeed. We agree that modeling the partial volume of each compartment (thin, thick and pale stripes) in each V2 voxel would be the most elegant approach. However, we note that z-scores between thin and thick stripe experiments may not reflect the voxel-wise partial volume effect, since they are a purely statistical measure and not a partial volume model. Having said this, we think that this general approach can give some additional insights and we provide results for a similar analysis here. We calculated the weighted sum of R1 and R2 values over all V2 voxels for each stripe compartment (thin, thick and pale stripes) independently (see above figure). For R1, we see the same pattern of R1 between stripe types as in the manuscript (Figure 5). Additionally, we show the differences here for each subject, which further demonstrates the reproducibility across subjects in our study. For R2, no clear pattern across subjects emerged, confirming the results in our manuscript. Since, this analysis did not add relavant new information to the manuscript, we refrained from adding this figure to the manuscript, in order not to overload it.

(2) In our current study, we were not primarily interested in investigating differences between thin/thick stripes and pale stripes. While histological analysis found differences (though not consistent) between CO dark stripes (more myelinated, (Tootell et al., 1983)) and CO pale stripes (more myelinated, Krubitzer and Kaas, 1989)), no study stated myelin differences between CO dark stripes. This does not fully exclude the possibility of myelination differences but suggests that if myelination differences between CO dark stripes existed, they would presumably be smaller than differences between CO dark and CO pale stripes. Thus, it would be even more difficult to demonstrate than the hypothesis of this manuscript.

Therefore, we decided to directly test two compartments against each other instead of modeling all three compartments within a single model. In our analysis, we thereby loosely followed the analysis methods described in Li et al. (2019), which compared myelin differences between thin/thick and pale stripes in macaques. We note that this demonstrates further consistency, since it is not trivial that both thick and thin stripes show lower R1 values than the pale stripes. For example, there may be no or opposite differences.

(3) Just for clarification, the plots in Figure 5 show the comparison of R1 (or R2*) between two compartments in V2. The red (blue) curve includes the thin (thick) stripe of interest. The gray curve includes everything in V2 minus contributions from thick (thin) stripes of interest. If we take the thin stripe comparison as example (Figure 5a), then red contains the thin stripes of interest while gray contains everything minus the thick stripes. Therefore, assuming a tripartite stripe arrangement, the gray curve contains both thin and pale stripe contributions.

References

Carey D, Caprini F, Allen M, Lutti A, Weiskopf N, Rees G, Callaghan MF, Dick F. Quantitative MRI provides markers of intra-, inter-regional, and age-related differences in young adult cortical microstructure. Neuroimage 2018; 182:429–440.

Dumoulin SO, Harvey BM, Fracasso A, Zuiderbaan W, Luijten PR, Wandell BA, Petridou N. In vivo evidence of functional and anatomical stripe-based subdivisions in human V2 and V3. Sci Rep 2017; 7:733.

Freund P, Seif M, Weiskopf N, Friston K, Fehlings MG, Thompson AJ, Curt A. MRI in traumatic spinal cord injury: from clinical assessment to neuroimaging biomarkers. Lancet Neurol 2019; 18:1123–1135.

González de San Román E, Bidmon H-J, Malisic M, Susnea I, Küppers A, Hübbers R, Wree A, Nischwitz V, Amunts K, Huesgen PF. Molecular composition of the human primary visual cortex profiled by multimodal mass spectrometry imaging. Brain Struct Func 2018; 223:2767–2783.

Kirilina E, Helbling S, Morawski M, Pine K, Reimann K, Jankuhn S, Dinse J, Deistung A, Reichenbach JR, Trampel R, Geyer S, Müller L, Jakubowski N, Arendt T, Bazin P-L, Weiskopf N. Superficial white matter imaging: Contrast mechanisms and whole-brain in vivo mapping. Sci Adv 2020; 6:eaaz9281.

Krubitzer LA, Kaas JH. Cortical integration of parallel pathways in the visual system of primates. Brain Res 1989; 478:161–165.

Lazari A, Lipp I. Can MRI measure myelin? Systematic review, qualitative assessment, and meta-analysis of studies validating microstructural imaging with myelin histology. Neuroimage 2021; 230:117744.

Lazari A, Salvan P, Cottaar M, Papp D, Rushworth MFS, Johansen-Berg H. Hebbian activity-dependent plasticity in white matter. Cell Rep 2022; 39:110951.

Li X, Zhu Q, Janssens T, Arsenault JT, Vanduffel W. In Vivo Identification of Thick, Thin, and Pale Stripes of Macaque Area V2 Using Submillimeter Resolution (f)MRI at 3 T. Cereb 2019; 29:544–560.

Mancini M, Karakuzu A, Cohen-Adad J, Cercignani M, Nichols TE, Stikov N. An interactive meta-analysis of MRI biomarkers of myelin. Elife 2020; 9:e61523.

Natu VS, Gomez J, Barnett M, Jeska B, Kirilina E, Jaeger C, Zhen Z, Cox S, Weiner KS, Weiskopf N, Grill-Spector K. Apparent thinning of human visual cortex during childhood is associated with myelination. PNAS 2019; 116:20750–20759.

Tootell RBH, Silverman MS, De Valois RL, Jacobs GH. Functional Organization of the Second Cortical Visual Area in Primates. Science 1983; 220:737–739.

Weiskopf N, Edwards LJ, Helms G, Mohammadi S, Kirilina E. Quantitative magnetic resonance imaging of brain anatomy and in vivo histology. Nat Rev Phys 2021; 3:570–588.

Whitaker KJ, Vértes PE, Romero-Garcia R, Váša F, Moutoussis M, Prabhu G, Weiskopf N, Callaghan MF, Wagstyl K, Rittman T, Tait R, Ooi C, Suckling J, Inkster B, Fonagy P, Dolan RJ, Jones PB, Goodyer IM, NSPN Consortium, Bullmore ET. Adolescence is associated with genomically patterned consolidation of the hubs of the human brain connectome. PNAS 2016; 113:9105–9110.

Author Response

Reviewer #1 (Public Review):

1) In family 2, the variant was detected by routine trio-based WES diagnostics. Sanger confirmation was not performed. IGV images can be added as supplementary material. Furthermore, median coverage was 75× which might not be sufficient for the identification of all heterozygous variants.

We thank reviewer for pointing it out for clarification. Obviously, at the time (2016) of the reporting of this variant this was our laboratory’s thoroughly validated protocol, which shows that median (!) coverage of 75x with the technology at the time is more than sufficient for robust variant calling. This particular variant was actually below 75X in coverage (at 65x), but Sanger confirmation was not necessary (based on thorough validation of the robustness of calling and GATK scores and other quality parameters for de novo calling). In addition, when coverage goes below 30-35X Sanger confirmation is warranted.

2) Proband 2 (P2) was born as the second child of non-consanguineous parents of Caucasian descent after an uneventful pregnancy and delivery. The boy was macrosomic at birth. Since there was macrosomia, how would the pregnancy be uneventful? At the last assessment at 10 years of age, obesity associated with hyperphagia was of concern; the weight of the patient should be clarified. P2 was diagnosed with autism spectrum disorder but a normal cognitive profile. The identified NM_001014809.2(CRMP1_v001):c.1280C>T variant is very rare and reported in GnomAD exomes with allele frequency 0.0000041.

Routine echographia during pregnancy did not result in any concerns. The pregnancy was indeed uneventful. BMI at last evaluation was 26.1. We included the details in the revised manuscript.

3) Proband 3 (P3) is the first of three children of a non-consanguineous family of European descent. There is a familial history of obesity on both parental sides, and the father is macrocephalic (head circumference: 60.5 cm). Macrocephaly can be isolated and benign, such as in benign familial macrocephaly. However, P3 presented with moderate intellectual disability and an autism spectrum disorder. Since P3 has a macrocephaly also, the PTEN gene should be further interrogated by detailed WGS data analysis as well as an additional orthogonal method(s) since it has pseudogenes.

We have not noted any pathogenic variant of the PTEN gene in the genetic analysis.

Reviewer #2 (Public Review):

Weaknesses of the article include:

1) Spelling errors and difficult-to-understand language. The use of "variant" is now preferred over mutation. According to current nomenclature, predicted but not experimentally confirmed protein alterations should be written as p.(Phe351Ser) rather than p.Phe351Ser.

We apologise for the spelling errors and the difficult-to-understand language in the manuscript. We considered the reviewers comments seriously and corrected the errors and rephrased the sentences wherever necessary.

2) Inconsistent use of in silico pathogenicity predictors and conservation metrics. These should be standardized for each case and should include at least phylop, CADD, and REVEL.

We have applied consistency in the description of in silico pathogenicity predictors and conservation metrics for each patient.

3) CRMP1 is under significant constraint against loss-of-function variation in gnomAD - pLI = 0.99, LOEUF 0.28. Genes in the top decile are highly enriched for haploinsufficiency as a disease mechanism. This should be considered in the interpretation of this data and incorporated into the manuscript.

We thank the reviewer for the comment. As per reviewer’s suggestion, we have included a statement in the revised manuscript under ‘Subjects and Methods’ section.

4) I am not convinced the data supports a dominant-negative interpretation. The variants do not oligomerize as well as wild-type CRMP1, and when co-expressed with wild-type CRMP1 there is an increase in monomeric wild-type CRMP1. While this could support a dominant-negative interpretation, an alternative explanation is these are loss-of-function alleles that cannot oligomerize, and at the stoichiometry of this artificial overexpression system, this leads to increased monomeric wild-type CRMP1. The axonal outgrowth studies are more compelling, but without a loss-of-function control allele, it is difficult to interpret.

The experiments in Figure 2 should be replicated, quantitated, and their statistical significance confirmed.

We thank reviewer for raising concern about the experiment and interpretation of the data. We performed size exclusion chromatography experiments and included the data in the revised Figure 2. Unfortunately, we could not reproduce the experiments for Figure 2B. From our current experimental results, we prove that the CRMP1 variants affect the homo-oligomerization process.

Reviewer #3 (Public Review):

1) The major weakness is Figure 2, as it is not performed up to high standards like the rest of the paper. Panel A does not show any loading control and does not confirm. Panel B at 720 kDa band is not convincing. Results should be repeated with size exclusion chromatography and/or another method to determine molecular weight and should be quantified from triplicate experiments. Panel C is also not convincing and should be repeated to more carefully show results, and quantified.

We thank reviewer for this important concern raised on our Figure 2 experimental data. We addressed the comments in the revised manuscript. We performed size exclusion chromatography and presented the results in the revised manuscript and discussed accordingly in page 23-24.

Fig. 2A: This panel shows the recombinant CRMP1 wildtype and the variants from E-coli expressing system. We repeated the expression several times and obtained similar partially cleaved proteins. Fig. 2A is Coomassie Brilliant Blue staining. Protein size marker and loading control (BSA) were applied on the same gel as shown in Fig.2A original.

Fig.2B: Due to limited protein expression of T313M and P475L mutants, we could not repeat the gel-filtration experiments.

Fig. 2C, 2D: It is difficult to adjust the expression level of each construct (CRMP1 wildtype, T313M, or P475L) in HEK293T cells (input). Therefore, we measured the signal intensity of myc-IP band and input ratio of V5 blot in each condition. Fig. 2D shows the ratio from four independent experiments.

Author Response

Reviewer #1 (Public Review):

In this paper, Quiniou and colleagues show via orthogonal methods that human thymopoiesis releases a large population of CD8+ T cells harboring a/b paired TCRs that (i) have high generation probabilities, (ii) have a preferential usage of some V and J genes, (iii) are shared between individuals and (iv) can each recognize and be activated by multiple unrelated viral peptides, notably from EBV, CMV and influenza.

Major strengths of the paper

Quiniou et al. generated single-cell sequencing datasets of the earliest stages of TCR beta chain gene recombination. And then showed that a subset of them is highly clustered also having high generation probability.

They show that these T cells can bind multiple antigens, both via the use of public antigen-specific datasets as well as corroborating experimental TCR expression and binding essays.

Minor weaknesses

To what extent is TCR clustering and high Pgen and cross-individual sharing correlated? What is the Pgen of the sequences clustered with the high Pgen cells? Can you comment on the correlation between these three phenomena?

Indeed, there is a significant positive correlation between the Pgen and the number of connections among the clustered TCRs, as was reported in Fig.1F of the original manuscript. Furthermore, this correlation is true for both private and public TCRs, as was reported in figure 2B of the original manuscript.

To show the link between the three phenomena, we now have added two supplementary figures showing a high positive correlation between Pgen and the number of connections, and between cross-individual sharing and the number of connections, and to a lesser extent between Pgen and cross-individual sharing (Figure 2-figure supplement 4C and D in the manuscript supplementary information).

However, we would like to emphasize that the difference in the mean Pgen of the clustered and dispersed TCRs is of about 20-fold. This is a high difference for a biological process (and highly statistically significant), but a small one compared to the 10-log10 span of the Pgens of the two populations. Factually, what we observed is not that clustered sequences have a high Pgen, but that they have a higher Pgen than the non-clustered sequences. Yet, many CDR3s with high Pgen do not cluster, and vice versa, indicating that a high Pgen is not the only (nor most important) driver of clustering. We have now added these as Figure 1-figure supplement 3E-F of our revised manuscript.

In other words, to what extent is this surprising to see that highly clustered TCRs have higher Pgen and are more shared?

That for a given CDR3 there is a correlation between having a high Pgen and being public is not surprising as both suggest a positive selection during evolution. What is more surprising is that there are CDR3s forming large clusters that occupy over 20% of the repertoire and that co-cluster between individuals with different HLA, “indicating a convergence of specificities between individuals’ clustered repertoires”. This suggests a surprising selection process that could depend less on HLA than the “classical” selection.

These points are now better emphasized in the revised manuscript.

Potential Impact of the paper

This work highlights an intrinsic property of the adaptive immune response: to generate TCRs with high generation probability that can efficiently bind multiple antigens. This finding has, therefore important impact on drug discovery and vaccine design.

We thank the reviewer for his appreciation.

Reviewer #2 (Public Review):

This study analyses the T cell receptor (TCR) repertoire of double positive human thymocytes, and compares this to mature single positive CD8 cells. The first major finding is that the repertoire post-selection is enriched for groups of TCRs with high generation probabilitites, similar sequences, and for TCRs previously annotated for viral specificity. This data is clearly presented and convincing. The extent of analysis of the human thymocyte repertoire is still very limited, and the paper adds significantly to this important question.

We thank the reviewer for his appreciation.

The second major finding is much more controversial. The authors first investigate the publicly available databases and show that there is a substantial proportion of TCRs which have been annotated to multiple viral specificities, a fact which is well-known to the specialists in the field, but not previously addressed.

Indeed, we are not aware of reports disclosing “a substantial proportion of TCRs which have been annotated to multiple viral specificities”. Actually, one could wonder why “a fact which is well-known to the specialists in the field” is not mentioned and discussed in published articles? To us, it reveals that this point has been overlooked by immunologists as recently in Zhang et al, 2021 where authors aiming at identifying highly specific T cell clones with a new modelling approach, excluded all clones binding more than 1 peptide. Thus, it makes it important to report it, as we do. Furthermore, we would also like to emphasize that we do more than just reporting that some TCR have “been annotated to multiple viral specificities”. We show from a manual curation of public databases that (i) some TCR have been reported to bind to tetramers presenting peptides from unrelated viruses; (ii) that such TCRs co-cluster using Levenshtein distance or GLIPH2 based clustering method; and (iii) that some of these TCRs indeed recognize different, unrelated peptides without significant sequence homology upon re-expression in carrier T cells.

The authors acknowledge that this in silico analysis is mostly based on unpaired alpha/beta sequence data, and that the chain pairing may influence specificity. They, therefore, perform a number of functional assays, demonstrating examples of T cells which respond by interferon gamma production to more than one peptide.

We thank the reviewer for pointing to the fact that, beyond tetramer binding, we performed cumbersome functional studies to document polyreactivity.

The paper is mostly very clearly written and presented and provides some fascinating novel perspectives on T cell cross-reactivity.

We thank the reviewer for his appreciation

The findings will surely be of interest to a broad readership - indeed anyone interested in how adaptive immunity works.

The link between the different sections of the paper is the weakest aspect. The relationship between thymic selection and polyspecificity, and also the real relationship between in silico "cross-reactivity" as evidenced by multiple annotations and the functional polyspecific T cells remains unclear.

Our flow of reasoning/analyzing was as follow. As we were studying the thymic selection of TCR repertoires, (1) we discovered a massive clustering within these repertoires. As for thymocytes this cannot be accounted for by a history of immune responses, this triggered our attention and led us to analyze the properties of these TCRs. This led us (2) to discover in these thymic repertoires “TCRs which have been annotated to multiple viral specificities”, that we were not aware of. We were so much intrigued by these observations that we wanted to substantiate them using datasets of paired  TCRs. As (3) we could confirm these observations in such datasets, this led us (4) to investigate these TCRs in functional studies. This is the link for the 1-to-4 sections.

To make this link clearer, we have reworked the titles of the different Results’ sections such as to emphasize the switch from thymocyte bulk sequencing studies to that of single peripheral cell sequencing studies.

The mechanistic molecular details underlying polyspecificity also remain unclear.

Indeed, we believe that solving the structure of polyreactive TCRs interacting with different peptides will be needed for a molecular understanding of polyreactivity, but that it falls beyond the present work.

But overall, lots of interesting new data, and some very intriguing hypotheses for the community to follow up on.

We thank the reviewer for his overall comment

Reviewer #3 (Public Review):

In this manuscript, the authors propose that there is a special, previously unrecognized, high-frequency population of a/b TCRs that are shared between people, have high generation probabilities, and react to many unrelated viral epitopes. Here is the main flow of the results, with comments on the strengths of the conclusions:

"Thymopoiesis selects a large and diverse set of clustered CDR3s with high generation probabilities" -- this seems correct and has been noted in earlier work by Mora and Walczak and others.

So far, Mora and Walczak selection models in humans are based on studying PBMCs (our ref n° 27 in the revised version), not thymic DP and SP sorted cells, even in the mouse derived models for which they used the total thymic cells (our ref n° 27).

Selection leads to a focusing of the CDR3 length which likely increases the degree of clustering and increases Pgen.

To address this question, we compared the CDR3 length distribution between DP CD3+ cells and CD8 SP cells from our thymic dataset. We did not observe major changes. The distribution and the mean of CDR3 length for the two cell populations remained identical. We only observed a small shifting in the CDR3 length distribution towards shorter sequences post-selection. This is now reported in the new Figure 1-figure supplement 3C in the revised manuscript.

"Clustered CDR3s are enriched for publicness " This also seems correct and again it makes sense: publicness is equivalent to having been independently rearranged (and sequenced) in another individual, which is determined by Pgen, and clustering is also determined to a large extent by Pgen (the factors that contribute to Pgen, shorter CDR3s for example, are largely shared between neighbor TCRs).

We agree that theory could have indeed predicted that. In any case, to our knowledge, this is the first report of large clusters of just selected thymocytes’ CDR3s that moreover co-cluster between individuals with different HLA.

"Clustered public CDR3s are enriched in viral specificities" -- This claim is not justified by the data, which comes from sequence matching against literature-derived databases. Rather, what is true is that "Clustered public CDR3s are enriched in public viral specificities".

We changed “CDR3s are enriched in viral specificities” for “clustered public CDR3s are enriched in public viral specificities".

But this might be a simple consequence of the previous observation, that "clustered CDR3s are enriched for publicness". One would need experimental specificity data on the very same datasets to make a conclusion about viral specificities in general.

We based our interpretation on experimental data.

Indeed, we manually curated databases to identify CDR3s that bind specific tetramers/dextramers. This type of “experimental specificity data” is for immunologists a paradigmatic and yet unchallenged mean to define specificity.

We make the observation that there are more CDR3s from a TCR that does bind tetramers/dextramers presenting viral peptides in clustered than in dispersed CDR3s. This is a highly statistically significant fact, that we now report as a fact that we leave open to discussion/challenge by our community.

"Identification of polyspecific TCRs" -- In this section, the authors report that some of the CDR3 clusters contain CDR3 sequences from literature-derived TCRs with multiple specificities. They conclude that these must represent polyspecific TCRs. The problem with this conclusion is that even having the same CDR3beta, let alone similar CDR3beta sequences, does not imply the same specificity. One can see the problem if one imagines a very deeply sequenced dataset, and focuses on a short CDR3 length with high frequency. With sufficient sampling, one will be able to navigate from nearly any single CDR3beta to any other CDR3beta of the same or similar length by jumping between single-mismatch variants. But this doesn't imply that all the TCRs from which these CDR3s were sampled, which likely have many different Vbeta genes and completely different TCRalpha sequences, must all bind the same thing.

We will first point to the fact that we did not analyze “a very deeply sequenced dataset”, but only the 18 000 most abundant sequences per sample. Singletons were excluded. In addition, we did not mean to say that all the connected TCRs have the same specificities, regardless of their position in the cluster. Clustering algorithms, whether LV distance of GLIPH2 for example, are now commonly used to infer specificity of clusters and it is admitted that the closer the TCR sequences are, the more they share their specificities.

That said, it is precisely because we acknowledge the limitation of bulk sequencing for inferring specificities that we turned to also analyze single-cell datasets.

We made this more apparent by the new sections of the results that more clearly indicate the shift from unpaired bulk thymocyte sequencing and paired single peripheral cell sequencing.

"Binding properties of polyspecific TCRs" -- Here the authors look to validate these results with paired TCR sequences. They analyze a public dataset made available by 10X genomics, featuring single-cell gene expression, TCR sequencing, and dextramer UMI counts for ~150,000 T cells. This is an amazing dataset with lots of interesting features, but, like any large high-throughput dataset, it needs to be analyzed with care.

We can assure the reviewer that we were always very careful. Actually, we even started by carefully reviewing the 10X proposed methodology, in which we identified major biases. This led us to explore this dataset cautiously and without preconceived ideas.

The authors claim to see evidence for large-scale cross-reactivity. This comes mainly from a set of dextramers for A03 and A11-restricted peptides. But these dextramers appear to be binding in a uniquely non-specific manner (by comparison with the other dextramers) and non-TCR-dependent manner in this experiment. One can see this, for example, by comparing the consistency of binding within expanded clonotypes: for a specific dextramer like A*02-GIL(Flu), positive binding for one cell in a clonotype greatly increases the likelihood of binding for other cells in the clonotype, suggesting that the binding is mediated by the TCR.

This is not true for the A03 and A11 dextramers (except for a few expanded clonotypes in an A*11 donor). TCR sequence doesn't appear to be the determining factor for binding to these dextramers; rather it may be expression of KIR genes or other surface proteins that can interact with MHC.

These are indeed striking binding patterns that are remarkably similar for a single CDR3 beta associated with more than 40 different CDR3s alpha (and moreover from two donors). The first attitude of immunologists would indeed be of discarding this observation for non-fitting the paradigms. We would like to rather propose an agnostic view at these results.

These results show that a series of five A03 and A11 dextramers loaded with various peptides bind to cells that express a given CDR3 beta associated with a multitude of CDR3alpha. If it would be an MHC to KIR binding, then such dextramers should bind to most cells, independently of their TCRs. We have added two supplementary figures (Figure 4-figure supplement 8B-C) to show that this is not the case, and that further show very different binding patterns.

If it would be a binding to “other surface proteins”, it would likely be the same.

We identified a CDR3 from donor 3 which binds preferentially to A03 and A11 dextramers. However, it binds to only 4 out of 5 of these. If the binding is non-specific and non-TCR-dependent, a binding for the A0301 RIAAWMATY BCL2L1 dextramer should also have been observed. Moreover, we identified this same CDR3beta in two other cells from donor 1 and 4, and that were associated with a different CDR3alpha. Except for only one binding, these TCRs didn’t show binding to the A03 and A11 dextramers.

Moreover, we identify another CDR3 from donor 1 that is associated with a strong binding to one A1101 dextramer presenting an EBV peptide when associated to many different CDR3alpha. The binding to the other A03 and A011 dextramer is weaker and seem to depend more on the CD3alpha.

If the binding of A03 and A011 dextramers is non-specific and non-TCR-dependent, why is there such a difference between the binding of A1101 IVTDFSVIK and A1101 AVFDRSDAK dextramers?

"Polyspecific T cells are activated in vitro by multiple viral peptides" Here the authors explore polyspecificity experimentally. First they report that polyclonal populations of T cells, sorted for binding to one dextramer, can also produce IFN gamma upon stimulation with a distinct peptide, albeit more weakly than for the cognate peptide.

This is indeed true for CMV+ sorted cells that respond better to CMV peptides than to EBV ones, but not true for EBV+ sorted cells that also respond better to CMV peptides than to EBV ones.

But it's not clear that the concentrations of the peptides are appropriate for stringently detecting cross-reactivity.

We wonder what does mean “stringently”? It is possible that stringently mainly means defining the conditions that eliminates what does not fit the current paradigm?

More factually, the peptide concentration used for these experiments, presented in Fig. 5A-B, was 1 µg/mL, i.e. ~1 µM for a 9-10 aa-long peptide. This is clearly a physiological concentration for viral peptides, routinely used in in-vitro recall assays. We can thus rule out that the observed cross-reactivity is simply due to an excess peptide stimulation.

Then the authors actually synthesize and characterize individual TCRs. Here what is seen is consistent with expectation and does not seem to support the idea of substantial fuzzy cross-reactivity: binding to the cognate peptide is 3-4 orders of magnitude stronger than to the alternative peptides.

We respectfully disagree. First, as shown in Fig. 5C TCR#35-13 (cognate peptide HLA-A2-restricted Flu MP 58-66) indeed recognizes the alternative HLA-A2-restricted CMV IE1 184-192 peptide with a 3-4 higher log EC50; yet, the EC50 of this TCR is approx. 10e-6 M, i.e. 1 µM, which remains a physiological concentration. Second, this is not the case for TCR#36-150 (same cognate peptide HLA-A2-restricted Flu MP 58-66), which actually recognizes the alternative HLA-A2-restricted EBV BMLF1 280-288 peptide with a 4-fold lower EC50.

The only exception is the GAD 114-122 TCR, where the different peptides appear to be closer in binding strength. But in this case, the authors state that they "analyzed their response to a set of peptides comprising their cognate peptide and peptides with no significant structural commonalities, selected by testing combinatorial peptide libraries". If the competitor peptides came from peptide library screening then the observation of strong binding to alternative peptides does not seem as surprising as a TCR that binds well to a Flu peptide, say, and also a CMV peptide, selected from a smallish set of possibilities.

As explained above, this TCR does not stand as an exception compared to Flu-reactive TCRs. Moreover, it should be noted that this GAD 114-122 TCR recognizes its cognate peptide in a similar or even lower concentration range compared to the Flu-reactive TCR #36-150. It should also be pointed out that, contrary to the Flu-reactive TCRs, here we did not have any reference dextramer binding data to guide our peptide selection, which is why we resorted to combinatorial peptide libraries. Thus, although different strategies were used, peptide selection was “guided” in both instances.

It is pretty well established that TCRs are cross-reactive, both for nearby peptides and also for sequence-dissimilar peptides.

We agree and had notably quoted the landmark paper by Don Mason estimating that each TCR may respond to over 106 different peptides from an estimated repertoire of > 1010 peptides. Based on the Don Mason estimate of cross reactivity, the chance to find a cross reactive peptide at random would be around 10-4.

Here, we just tested a few peptides from different viruses. If Don Mason’s estimates are correct, for a given TCR, the chance to find even just 1 cross-reactive peptide among these few peptides would be at most of 10-3, the chance to find 2 cross reactive peptides would be of 10-6 and that to find 3 or more cross reactive peptides would have be infinitesimal.

Thus, if the polyreactivity that we described is part of this general cross reactivity, our results are at least highlight a major previously unreported bias in the selection of these cells.

The question is whether widespread, functionally relevant (not just dextramer binding at some concentration) poly-reactivity to diverse viral peptides is a defining feature of a large fraction of the TCR repertoire. The paper does not appear to present sufficiently strong evidence to support this claim.

We agree with the reviewer that more work is needed to “fully” appreciate the role of polyreactive cells!

Author Response

Reviewer #2 (Public Review):

This paper reports a novel measure of biological age derived from machine-learning analysis of retinal imaging data with chronological age as the criterion measure. The resulting algorithm is impressive. Not only can the retinal image data accurately predict chronological age in the training data and record changes over short time intervals, but it also proves accurate in independent test data and appears to contain information related to mortality risk. In addition, the authors report a GWAS of the new measure.

I would like to see a bit more validation data in the UKB - how does EyeAge relate to (a) tests of visual acuity - e.g. does it explain aging-related differences?

We have extended the supplemental tables and figures (Supplementary table 5 and Figure 3- figure supplement 2) to show additional adjustments to the hazard ratios using visual acuity.

(b) measures of morbidity and disability - e.g. how is EyeAge Accel associated with at least some of the counts of chronic diseases, self-reported physical limitations, tests of physical performance, measures of fluid intelligence?

We felt that all-cause mortality is the most clear outcome to test against, as other outcomes were not available for all participants or would require domain-specific knowledge to properly incorporate which we felt was out of scope. Given this, we have added this limitation to the discussion:

“This study has several limitations. First, further work will be needed to assess whether eyeAgeAccel is correlated with other important health outcomes and measures.“

But overall, this is a very strong report of an exciting new biomarker of aging. It was unclear to me whether the algorithm to compute the measure would be publicly available. The authors should clarify.

Code for both training and evaluation of eyeAge from fundus images is available by minimally modifying open-source software we previously released under the permissive BSD 3-clause license. We have added the following “Code availability” section to the paper:

“To develop the eyeAge model we used the TensorFlow deep learning framework, available at https://www.tensorflow.org. Code for both training and evaluation of chronological age from fundus images is open-source and freely available as a minor modification (https://gist.github.com/cmclean/a7e01b916f07955b2693112dcd3edb60) of our previously published repository for fundus model training57.”

Author Response

Reviewer #1 (Public Review):

This is a very interesting paper trying to quantify excess deaths due to the COVID-19 pandemic in the USA. The paper is roughly divided into two main sections. In the first section, the authors estimate age and cause-specific excess mortality. In the second section, using their excess mortality estimates, the authors attempt to disentangle the impact of SARS-CoV-2 infection (direct impact) vs. the impact of NPIs on this excess mortality (indirect impact). I have some concerns, particularly with respect to the second section.

The model used to estimate excess mortality is quite clear. The authors adjust the baseline model to account for low influenza circulation (and deaths) during the COVID-19 pandemic, to avoid underestimating the number of deaths caused by COVID-19. While this makes sense if the authors are trying to estimate the total number of deaths caused by COVID-19, I'm not sure it needs to be accounted for if the authors want to estimate excess/added deaths. A counterfactual scenario would've included influenza. It also raises the question of whether (conceptually) they should be adjusting for other causes of deaths that may have also decreased during the pandemic. The authors briefly acknowledge this in the discussion ("we can't account for changes in baseline respiratory mortality due to depressed circulation of endemic pathogens other than influenza") but my comment goes beyond respiratory diseases. Analyses of excess mortality from other settings have suggested, for example, decreased deaths due to fewer traffic accidents (not in the US) or due to decreased air pollution, and not accounting for these would also lead to an underestimate of the total deaths caused by COVID-19. I understand that it is not feasible to account for all potential factors, so I wonder if they should focus on reporting excess deaths as compared to a counterfactual with influenza.

Thanks. We think it is helpful to “single out” influenza as it causes major fluctuations in mortality from multiple causes in regular years and is a useful reference to contrast the pandemic impact. But the reviewer’s point is well taken. We have clarified our assumptions about the meaning of the baseline in this analysis (methods p 5), discussed the depressed circulation of other pathogens in depth, and mentioned air pollution (p 12-13). We have also slightly reworked our comparison between COVID19 and influenza so that excess mortality estimates are comparable and now cover periods of the same duration (Nov 2017-Mar 2018 for flu and Nov 2020-Mar 2021 for COVID19, see Figure S11).

The second section, trying to estimate direct vs. indirect effects is also very interesting. However, more details are required about the regression model used and, importantly, what the assumptions and limitations of the approach are. Specifically:

• Please provide a bit more information on the regression used for direct vs. indirect effects. I'd like to see explicit discussion of the assumptions and limitations of the approach but also of the stringency index used. Does this model include an intercept? Was the association between stringency index and excess deaths assumed to be linear? Or were different functional forms considered? It is also not clear how well the model fits the data.

Thanks for these comments which helped us improve this section. We have provided more details about the stringency index in methods (it captures the “sum” of interventions), described the model in methods and supplement, and discussed limitations in caveats section, especially regarding effectiveness of these interventions (p13). We had tried different linear models with and without intercepts but elected to use models with intercepts so as not to overly constrain the relationship between interventions, COVID19 activity and excess mortality. These models also incorporate lags in the predictors that are determined by cross-correlation analysis (as detailed in supplement). In the revised version, we now use gam models, where the relationships between excess mortality and predictors do not have to be linear. We can do so since we were able to add several weeks of data (the regression is now based on 96 pandemic weeks from March 1, 2020 to January 1, 2022). The models are described in detail in supplement p 4-5, and we now specify that they have intercepts. We have also provided additional plots of model fits in main text and supplement (Figures 4 and S16-19).

• Related to the above, please provide more details on how the results of the regressions were translated into the results presented. The main text reports percentages, but the methods only briefly explain how numbers of direct deaths were calculated, and the supplementary tables report coefficients. It is not clear if these estimates of direct and indirect deaths were somehow constrained to add up to the total number of excess deaths, but it doesn't seem like it since point estimates cross 100% in some cases.

As discussed in response to one of the editor’s questions, estimates are not constrained to 100%. We have provided more details in the supplement on how we estimate the direct impact of the pandemic. Briefly, we calculate expected deaths in the gam model with all predictors set to their observed values and again with the COVID19 predictor to zero. The direct impact is the difference between the two predictions, divided by the predictions of the full model.

We note that while some of the estimates derived from gam model exceed 100% (and are similar to the linear model estimates presented in the initial analysis, before revision), these estimates echo the findings from a more empirical analysis, in which we compare all-cause excess deaths with official COVID19 deaths tallies. There, in the two oldest age groups, we find more official COVID19 deaths than estimated by the excess mortality models. Hence both analyses point to an underestimation of the direct burden of COVID19 by the excess mortality approach, specific to the oldest age groups. We return to this point in depth in the discussion (p 12-13) and consider the possible effects of harvesting, depressed circulation of non-SARS pathogens, and inaccurate coding of official statistics (as pointed by reviewer #3).

• Please discuss the potential limitations of using the stringency index to quantify NPIs.

Several limitations have been added to caveats (p 13); major issues include aggregation of multiple interventions into a single index, which does not consider the actual implementation nor the effect of interventions. The index is solely based on mandates in place in different locations and time periods. We also assume that the effectiveness of these interventions, for a given level of stringency, does not change over time.

• When estimating direct and indirect effects, the paper assumes that the estimated parameter is time-invariant? Indirect effects might have changed over the course of the epidemic by factors not necessarily captured by the stringency index used, particularly since the index doesn't take into account the implementation of the measures. Have the authors tested this assumption?

This is an interesting point, which we have explored further. The non-linear relationships we find between NPIs and chronic condition excess mortality may suggest that the reviewer is right. We discuss the role of NPIs in the results section much more deeply than we were previously (bottom of p8).

“At lower levels of interventions (Oxford index between 0 and 50), representing the early stages of the lockdown in March 2020, excess mortality rose with interventions. Later in the pandemic, increased interventions were estimated to have a beneficial effect on excess mortality, driven by comparison between the period when interventions were strengthened in response to increasing COVID19 activity in late 2020 (Oxford index above 60) to the period when interventions were relaxed in 2021 (Oxford index between 50 and 60).”

We cannot run an analysis over different time windows because NPI and time are highly conflated (for instance NPI rise from 0-50% in the very early part of the lockdown period, and then stays above 50% for the rest of the study, so we cannot compare the effect of a 25% level in 2020 and 2021). We have added this limitation in the caveat section p.13.

• The authors state "In contrast, the indirect impact of the pandemic measured by the intervention term was highest in youngest age groups, decreased with age, and lost significance in individuals above 65 years" - I'm not entirely sure of where this statement comes from? For example Table S3 suggests that the indirect effect (multivariate or univariate) is higher in 25-64 yo than in <25s? The same table also suggests negative impacts (protective effects?) in >75s in the multivariate model. Please clarify.

There are fewer deaths in the under 25 yo so this is why the coefficients were lower overall in table S3. Yet we find that the proportion of variance explained by interventions is higher in the under 25 yrs than in 25-44 yrs.

We have now changed our modeling strategy to use gam so Table S3 is no longer relevant but the main conclusion that interventions explain a larger relative portion of excess mortality in the under 25 yrs than in the other age groups, and than other covariates, remains valid. The NPI term is now significant is in all groups (although the relative contribution of NPI still declines with age, as in the prior analysis), so we have rephrased this sentence: “In contrast, the relative contribution of indirect effects, via the intervention variable, was highest in youngest age groups and decreased with age”.

• How do the authors interpret "Percents of excess deaths" over 100%? Similarly, I don't fully understand how to interpret "The upper bound of the 95% confidence interval for heart diseases was above 100% (158%), suggesting that for every excess death from heart disease estimated by our model, up to 1.58 death from heart disease could be directly linked to SARS-CoV-2 infection.

We have rephrased this section although the overall conclusions remain unchanged. GAM estimates of the direct COVID 19 impact is statistically significantly above 100% in the 85 yo and over, suggesting that our excess mortality approach is too conservative and does not estimate enough COVID19 excess deaths in this age group. We draw a similar conclusion from a more empirical analysis, in which we compare all-cause excess death estimates with official COVID19 deaths tallies. In this analysis, we find more official COVID19 deaths than estimated by the excess mortality models in the two oldest age groups (point estimates above 100% in the 75-84 and 85+ yrs). Hence both analyses point to an underestimation of the direct burden of COVID19 in the oldest age groups by excess mortality approaches.

Rephrased results section bottom of p.9: “We estimate that the direct contribution of COVID-19 to excess mortality increases with age, from negative and non-statistically significant in individuals under 25 yrs to over 100% in those over 85 years, echoing the gradient seen in official statistics (Table 4). It is also worth noting that our excess mortality estimates may be too conservative (too high) as we did not account for missed circulation of endemic pathogens. This could explain why our estimates of direct COVID-19 contribution exceed 100% in the oldest age group.“

We return to this point in depth in the discussion and consider the possible effects of harvesting and depressed circulation of non SARS pathogens (p 12-13).

• Table 3: The signs of the point estimate vs CI for vehicle accidents are inconsistent.

Thanks, this was a typo. It should have been 4300 (-700, 9300) excess deaths from accidents. This has been updated with more recent data.

Reviewer #3 (Public Review):

Authors examine mortality data in the US and use time-series approaches to estimate excess mortality during the COVID-19 pandemic.

Major comments:

I would encourage authors to discuss the two different concepts of excess mortality:

(#1) what deaths were caused, directly or indirectly, by the pandemic. This is what the authors have aimed to assess, and I have no major concerns with the methodology

(#2) how many additional deaths occurred during the pandemic, compared to what would have been expected in the absence of a pandemic. For such an analysis I think expected annual influenza deaths should be added back to the baseline (or subtracted from the excess)? Some of the discussion seems to relate more to an impression of #2 rather than #1 but I would be interested in the authors' thoughts.

We have added more details about the approach, in particular why we think that #1 is the proper analysis here (see methods p 5). Given the sheer magnitude of COVID19 excess deaths (over 1 million excess deaths at the end of our study), adding back influenza deaths (up to 52,000 deaths in a recent severe season with a mismatched vaccine, as in 2017-18) would not make a large difference. We have also provided a more direct comparison of the impact of influenza and COVID19.

1. Authors estimate fewer excess COVID deaths in the elderly than there were confirmed deaths (Table 3). Could this be an indication of some confirmed deaths being "deaths with COVID" rather than "deaths from COVID"? I'm not sure how to interpret the %s in the final column when they exceed 100%. The authors suggested a harvesting effect but I would suggest "deaths with COVID" might be a more likely explanation? This issue can be a limitation of confirmed-death data.

This is a good point. We have added a comment along these lines in discussion in the middle of p 12. Still, we think harvesting and/or the depressed circulation of endemic pathogens, which would have inflated our baseline, are more likely explanations for these findings. This is because we find similar estimates (exceeding 100%) in gam models that ignore official statistics and rely on COVID19 case data, or COVID19 hospital occupancy data, and this suggests that other mechanisms, beyond coding of official mortality statistics, are at play.

Yet, as more detailed official statistics become available, a tabulation of confirmed deaths by presence of a primary vs secondary COVID (U07) code may be revealing and get more directly at the reviewer’s question.

Author Response*

Reviewer #1 (Public Review):

ARL3 is a small GTPase that localizes to the primary cilium and plays a role in regulating the localization of some specific ciliary membrane proteins, including PDEδ and NPHP3. Mutations in this gene cause Joubert syndrome, a type of ciliopathy characterized by cerebellar malformation, and retinal degeneration. While the majority of the diseases occur in an autosomal recessive manner, two mutations in ARL3 (D67V and Y90C) have been reported to cause autosomal dominant retinal diseases. In the current paper, Travis et al. sought to understand the pathogenesis of the diseases caused by the two autosomal dominant mutations. They found that D67V acts as a constitutive active mutation, whereas Y90C is a fast-cycling mutant, which can be activated in a guanine nucleotide exchange factor (GEF) independent manner. Since the fast-cycle mutant did not bind to the effector proteins in vitro (likely because the guanine nucleotide falls off from the mutant ARL3, which has a lower affinity to GDP/GTP), they developed a method to snapshot the interaction between ARL3 and its effector. Using this method, they showed that the Y90C mutant indeed has increased interaction with the effectors, suggesting that Y90C is an overactive form of ARL3. They then addressed how photoreceptor cells are affected by these two mutations using a mouse model and found that the mutations disrupt the proper migration of the photoreceptor cells.

Strengths:

• The paper is well written, and it was easy to understand what the authors did from the figure legends and the methods section.

• It was easy to find out what is known or unknown, as the paper has accurate references.

• The authors developed a method to analyze a snapshot of the interaction between ARL3 and its interactors.

• The paper has an in vivo model and connects the biochemical characteristics of ARL3 to in vivo cellular phenotypes.

Weaknesses:

(1) I understand that authors focused on nuclear migration defect as the phenotype was first described in ARL3-Q71L transgenic mice. The similar phenotype observed in RP2 knockout mice further supports the idea that the defect is caused by the hyperactivation of ARL3. Indeed, the defect is not reported in the ARL3 knockout mice, however, I feel that it does not necessarily mean that the defect is not caused by loss of function. Although it has not been assessed, ARL3 knockout mice might have the same defect. Therefore, I think analyzing both the migration defect and trafficking defect would be more informative, rather than focusing on the migration defect. The fact that the relationship between nuclear migration defect and the retinal degeneration phenotype is not entirely clear further enhances the importance of analyzing the trafficking defect.

Does the expression of ARL3-Y90C also cause the trafficking defect? If it is the case, you can separate the nuclear migration phenotype from the one caused by the trafficking defect. Would the expression of lipidated cargo(s) rescue the trafficking defect as well?

I think many questions can be addressed by analyzing the localization of the lipidated cargos, such as PDEδ and GRK1.

The effect of Arl3-Y90C expression on trafficking of lipidated cargos is an interesting question. Previous papers showed mislocalization of lipidated outer segment proteins in Arl3-KO rods and down-regulation or subtle mislocalization in Arl3-Q71L overexpressing rods. So, this was one of the first things we investigated; however, we never observed mislocalization of ciliary or outer segment lipidated cargos (i.e. GRK1, transducin, Rab28, and PDE) in wild type mature rods that were overexpressing Arl3 mutants, and many were tested. It was through these experiments that we first identified the pronounced nuclear migration defect. Rod photoreceptor nuclear migration is a developmental process that is completed by P10, so Arl3-Y90C overexpression is causing a developmental defect. When rods are positioning their nuclei in the ONL, they are still “immature” as their primary cilium has not begun to elaborate disc membranes for light capture. All our analysis was performed in mature rods, so it is not surprising that we did not observe any lipidated trafficking defects at this timepoint. Since the developmental timing of the nuclear migration defect is important for our manuscript, we have added this to our introduction. Additionally, we use “immature” photoreceptors for the cartoon diagrams showing how Arl3 activity is altered by different mutation and rescue experiments, since formation of the mature outer segment occurs post-migration.

(2) I am not quite sure if the nuclear migration was assessed properly. Based on the pictures in Fig.1, some of the FLAG-negative cells also seem to be migrating to INL (please see Fig.1C and Fig.1D). Is this biologically normal during development? Could this analysis be affected by the thickness of OPL, the layer between ONL and INL? Also, the picture is cut out in the middle of INL. Could authors include more layers, such as IPL, of the retina in the picture, so that we can evaluate INL and OPL better? Taking this into account, I think it is worth measuring the nuclear position of FLAG-negative cells as a negative control in all the experiments.

Our electroporation technique results in a small population of rods that express our constructs of interest (~5-15% with a patch). All the experiments were performed in wild type retina which develop normal retinal layers, so analysis of the nuclear position of FLAG-positive cells with the retina is cell autonomous. Migration defects are assessed by differences in the skew of FLAG-labeled rods relative to the boundaries of the wild type ONL, which is marked by Hoechst nuclear stain (also a measure of the FLAG-negative rods). Wild type photoreceptors nuclei are not found within the INL, the nuclei in that layer belong to either horizontal cells or bipolar cells both of which are not targeted by our electroporation approach. As a control, we show that when wild type Arl3-FLAG was expressed FLAG-labeled rods were never observed within the INL. We have now included the % of displaced nuclei in Table 1.

(3) The way that the authors showed the Y90C mutant of ARL3 is a fast-cycling mutant is not very compelling. In Figure 2C, the authors showed that ARL3 Y90C can bind to PDEδ, its effector, once it is pre-loaded with GTP. The authors also showed that the mutant can bind to its effector even without EDTA as long as an excess amount of GTP is added. The authors used endogenous ARL3 as a control to compare the effects between wild-type and mutants. I see that this experiment has multiple pitfalls. First, ideally, this type of experiment needs to be done with a purified protein using fluorescent guanine nucleotide/radioactive guanine nucleotide (e.g. nucleotide loading assay or nucleotide exchange assay) to directly access the kinetics of nucleotide exchange. However, I do understand that this is out of the authors' expertise. In the authors' experimental setting, I am not sure loading the protein with GTP in the presence of the EDTA means anything more than confirming that the protein is intact. Theoretically, wild-type and a fast-cycling mutant can load GTP with similar efficiency in the presence of EDTA. Then during immuno-precipitation, GTP falls off from the Y90C mutant faster than wild-type (because a fast-cycling mutant theoretically has a lower affinity to guanine nucleotides), assuming that GTP was not added during immuno-precipitation (GTP addition was not mentioned in the method, but could authors confirm this?). But in this case, the kinetic of GTP dissociation can be affected by many factors, including the presence of GAP in the reaction, the dissociation constant of Y90C, the volume of the buffer used, and the number of washing steps. Thus, it is not very easy to estimate the difference between wild-type and Y90C. Besides, using endogenous ARL3 rather than ARL3-wild type FLAG as a control can be dangerous. I have experienced that a tagged protein is cleaved to a protein that has a similar size to endogenous protein. (I expressed GFP-protein X in knockout cells lacking protein X, and saw the band at the position where the endogenous protein is observed in wild-type cells). So, the endogenous band that the authors showed could come from the cleaved FLAG-Arl3. (Authors can easily confirm this by having wild-type not expressing FLAG-tagged ARL3, though).

An alternative experiment that I would suggest is doing immuno-precipitation in the buffer containing: 1) no guanine nucleotide, 2) 10mM GDP, or 3) 10mM GTP in the cells expressing the following protein: 1) ARL3 wild-type FLAG, 2) ARL3 Y90C FLAG, or 3) ARL3 D129N FLAG. 10mM guanine nucleotide should be added throughout the process including washing. This experiment might also be affected by many factors, but variability should be lower than the experiment presented in Fig 2C. ARL3-wild type FLAG is also a better control here than endogenous protein.

Variability due to the factors you mention is a concern, but we were able to repeatedly obtain the same results using our method—admittedly our method is testing whether the mutated Arl3 can exchange under a certain condition more than exactly how. We know that we are not providing precise kinetics or elucidating the underlying mechanism for how these mutations lead to what we are calling fast cycling. While that information is important, it is outside the scope of this paper.

As you mention, an important conclusion from the PDEδ binding experiments is that we confirm the Arl3-Y90C protein is intact by showing it can indeed bind nucleotide as long as there is an excess of GTP (Fig 2B. The interesting finding from these experiments is that Arl3-Y90C binds GTP even in the presence of magnesium, a behavior not observed for wild type Arl3. We feel that showing that endogenous Arl3 is not activated in the presence magnesium in each of our preparations is a lovely internal control. However, we agree that showing wild type Arl3-FLAG in these assays is an important negative control and have now included this blot as Fig 2-Sup Fig 1.

(4) In Fig.3, the authors attempted to take a snapshot of the interaction between ARL3 and multiple effector proteins. The three bands that were enriched in the Q71L cells were found as RP2, UNC119, and BART by mass spec (Fig.3B). These bands were used as a readout for the subsequent experiments. I am not quite sure why the authors used this approach rather than using the cell line that expresses both FLAG-ARL3 and GFP tagged protein of interest, just like what the authors did in Fig3G. The reasons why I prefer the latter approach are the following: FLAG bands that correspond to the three proteins (RP2, UNC119, and BART) in wild-type cells are very close to the detection limit, 2) authors failed to confirm that the lowest band actually comes from BART, 3) authors cannot access some important effector proteins, such as PDEδ because 293 cells might not express them. All of the problems can be solved by using the approach that was taken in Figur 3G.

If the authors chose the former approach because of some specific reason, I would appreciate it if the authors could explain that in the main text of the paper.

In vitro crosslinking experiments were performed to test whether overexpression of Arl3 mutants resulted in an active cellular Arl3 without artificially changing any components of the GTPase cycle. We feel these experiments are highly elegant as they allow us to take a snapshot of native Arl3 activities without compromising the analysis by artificially altering GAP/GEF/effector interactions through overexpression or during lysis (as we show that the concentration of GTP/Mg could alter interactions in Fig 2). While AD293T cells are not rod photoreceptors, we are able to use this system to better understand how the Arl3 mutants alter the level of activity within the cell. Yes, this experimental assay is novel, but we confirmed the identity of the effectors by Western and mass spec, used positive and negative controls in each experiment, and show that the method is highly reproducible. We agree with Reviewers 2 and 3 that using this method to study the cellular activity of fast cycling Arl3 mutants is a strength of our paper.

(5) ALR3 Y90C causes nuclear migration defect. Given that Y90C is a fast-cycling mutant (hyperactive) and has a high affinity to ARL13B, the nuclear migration defect might come from either the increased activity of ARL3 or sequestration of ARL13B, which can act as a GEF for ARL3 but potentially have other functions. If my understanding is correct, the authors concluded that the defect caused by ARL3-Y90C is likely due to hyper-activation of the protein, as Y90C/T31N mutant, which cannot bind to effectors but still retains the ability to capture ARL13B, did not cause migration defect. But I am a little confused by the fact that Y90C/R149H, which is unable to bind to ARL13B (Fig.2C) but still retains the ability to interact with the effectors (Fig.3F), did not have migration defect (Fig.7B). Wouldn't this mean that the sequestration of ARL13B could contribute to the phenotype?

If my understanding is correct, the authors are trying to say that both hyper-activation of cytosolic ARL3 and the defect in endogenous ARL3 activation in cilium is necessary to cause migration defect. I am not very convinced by this hypothesis, and still think that the defect could be caused by sequestration of ARL13B to the cytoplasm.

Then why Y90C/T31N did not cause the defect even though they can sequester ARL13B? This might be explained by the localization of the ARL13B mutants. If Y90C can localize to the cilium while the double mutant, Y90C/T31N, does not, then only Y90C might be able to inhibit the ARL13B function in the cilium. This could explain the lack of the defect in the cells expressing Y90C/T31N.

It would be helpful to understand how exactly the fast-cycling mutant causes the defect if the authors can provide more information, including localization of ARL3 (wild-type and mutants) as well as key proteins, such as ARL13B and the effector proteins. Assessing ARL13B defect seems to be particularly important to me because ARL13B deficiency has been connected to neuronal migration defect (Higginbotham et al., 2012)

What I am trying to say here is that how the defect is caused is likely very complex. So, providing more information without sticking to one specific hypothesis might be important for readers/authors to accurately interpret the data.

Our data shows that for the fast cycling Arl3-Y90C mutation both features: blocking endogenous Arl3 activation in the cilium (through Arl13B binding) and increasing activity of Arl3-Y90C in the cell body are required to produce a nuclear migration defect. We find that we can rescue migration defects by either restoring activation in the cilium or reducing GTP activity outside the cilium. As long as there is more Arl3-GTP activity in the cilium, then the rod can handle aberrant Arl3-GTP activity in the cell body. The Y90C/R149H was a critical result that led to our hypothesis that there is a gradient between the two compartments that is used for proper migration. One interesting point is that absence of any activity does not produce the migration phenotype, further suggesting that an imbalance in the gradient is important.

We performed new experiments to investigate whether Arl3-Y90C is sequestering Arl13B away from the cilium but found that localization of Arl13B (both endogenous and overexpressed) is not altered by expression of Arl3-Y90C – see Fig 3-SupFig 1-2.

It is an interesting question as to how different Arl3-FLAG constructs are localized within the photoreceptor. Sadly, we did not analyze the data in a way that would allow us to draw any conclusion about the localization of different Arl3-FLAG constructs. In general, we observed FLAG localization throughout the photoreceptor cell and focused our imaging on the FLAG staining around the nucleus so we could further analyze ONL position. Looking back through our images, some of mutants might have a more prominent localization within a specific subcellular compartment (e.g. Arl3-D67V is more prominent in the inner segment than outer segment and Arl3-Y90C appears to have dominant outer segment localization). Likely, these differences represent each mutant binding a particular effector: D67V to RP2 and Y90C to Arl13B, which we show biochemically. Ideally, Arl3 mutant localization would be analyzed during development to provide a more direct link to the nuclear migration defect, a future direction for our lab. We have updated our manuscript to be more transparent about the potential differences in rod localization of Arl3 mutants.

(6) The rescue experiments that the authors presented in Fig.5-6 are striking and would build a base for future therapy of the diseases caused by ARL3 defects. However, I believe more examinations are needed to accurately interpret the data. The authors did this rescue experiment by co-injecting ARL3-FLAG and chaperons/cargos if I understand the method section correctly. But I feel we can interpret this data correctly only when ARL3-FLAG and chaperons/cargos are co-expressed in the same cells. I think a better way to analyze the data might be by comparing the nuclear migration phenotype between ARL3-FLAG only and ARL3-FLAG;chaperons/cargos double-positive cells.

Our lab has found that the initial estimates by the Cepko Lab that co-injection of two plasmids results in above 90% of rods expressing both proteins is accurate (see reference Matsuda and Cepko PNAS 2004). Since we only assess nuclear position of FLAG-labeled rods, it is true that a small percentage of cells in this analysis express the Arl3-FLAG mutant and not the chaperone/cargo; however, inclusion of these cells really only bolsters our findings as complete rescue would likely be even more robust than measured.

Reviewer #2 (Public Review):

The small GTPase Arl3 (Arf-like 3) is a well-characterized component of primary cilia, including the outer segment of photoreceptors, which contain specialized cilia. Arl3 is critical for the import of multiple lipid-modified proteins into cilia that are vital to ciliary function. Human mutations in Arl3 are reported to cause both autosomal recessive and dominant inherited retinal dystrophies, but the mechanisms through which these mutations disrupt photoreceptor development are not known. Here the authors show that two dominant Arl3 mutants, Arl3-D67V and Arl3-Y90C exhibit increased activity, but for different reasons. Arl3-D67V is constitutively active (unable to hydrolyze GTP), whereas Arl3-Y90C is a classic rapid-cycling mutant, able to bind GTP spontaneously (independent of its guanine nucleotide exchange factor Arl13) but still able to complete the GTPase cycle by hydrolyzing GTP. Expression of either mutant in developing murine retinas results in a nuclear migration defect, specifically aberrant localization of rod nuclei to the inner rather than outer nuclear layer. In this sense, they phenocopy another well-characterized constitutively active mutant, Arl3-Q71L. Normal nuclear distribution could be restored by overexpression of Arl3 effectors, suggesting that the active mutants disrupt nuclear migration, at least in part, by sequestering Arl3 effectors.

While the data are reasonably clear and convincing, there are several instances where the conclusions drawn are either confusing or problematic. Specifically:

1) Although retinal rod cells are ciliated in their outer segment, the authors never actually examine ciliation here. Their only morphological readout is nuclear migration. How does nuclear migration failure impact ciliogenesis in the outer segment?

Imaging was performed in mature retinas at P21 after outer segment formation is completed. Electroporation only targets a small population of cells for which we observed normal outer segments structures in all conditions tested — therefore we conclude that ciliogenesis is unaffected. Previous literature has also showed that defects in rod nuclear migration do not affect ciliation of the outer segment.

2) The Arl3-Y90C mutant seems to act physiologically more like a dominant-negative than an activated mutant. A second mutation in Y90C (R149H) that blocks binding to the GEF Arl13 abrogates the nuclear migration defect, suggesting that Y90C is preventing activation of endogenous Arl3 by sequestering the GEF. Yet overexpression of effectors or cargos still rescues nuclear migration in the presence of Y90C, suggesting that it also sequesters effectors. How do the authors explain this?

We agree with this interpretation. We have now included language about Arl3-Y90C’s role as a dominant negative in that it blocks Arl13B activity. The interesting caveat to this black and white usage is that blocking Arl13B would suggest a reduction in endogenous Arl3 activity in rods (which we find to be true, see Fig 5A). However, the migration defect phenotype mimics overly active Arl3 (Arl3-Q71L) and not a loss of function in Arl3 (Arl3-T31N). Using in vivo crosslinking experiments, we show that the fast cycling nature of Arl3-Y90C also causes GEF-independent activation of Arl3 (Fig 4D-E) that leads to the migration defect. Our rescue data shows that only the combination of both effects – reduced Arl3 activity in the cilium and GEF-independent Arl3 activation outside the cilium - is enough to disrupt the ciliary gradient and produce the migration defect.

3) Fig. 1 suggests that an Arl3-T31N mutant has no phenotype. This is a canonical mutation in small GTPases that typically renders them dominant negative. The lack of phenotype is surprising since most dominant-negative mutants act by sequestering their GEFs, thereby preventing activation of the endogenous GTPase. Fig. 2C suggests that this may not be the case for Arl3-T31N, which binds Arl13 only weakly. Some of this confusion may arise from the fact that Arl13 is not a typical GEF. It is very unusual for one GTPase to directly promote nucleotide exchange on another. Does Arl3-T31N affect ciliation in the rod outer segment, or in other ciliated cells? Some discussion of this point is warranted here.

Our paper finds that Arl3 mutants must produce an aberrant activity outside the cilium, whether through constitutive activity (seen for D67V and Q71L) or fast cycling (seen for Y90C and D129N) to cause the migration defect. Since T31N does not cause excess Arl3 activity in cells (see Fig 4) even if it does have some dominant negative activity toward Arl13B, then it is still not enough to cause the migration phenotype. This was directly tested in Fig 5, where we increase T31N binding to Arl13B by introducing Y90C/T31N and still do not see migration defect. Our results are also in line with a previous study showing that despite rapid photoreceptor degeneration in a retina-specific conditional Arl3 knockout mouse the outer segments were initially formed, in contrast the retina-specific conditional Arl13B knockout mouse did disrupt photoreceptor ciliogenesis leading to a more rapid degeneration (Hanke-Gogokhia, JBC 2017). Since complete loss of Arl3 activity did not disrupt ciliogenesis, it is unlikely that expression of Arl3-T31N in wild type retinas would alter outer segment formation, and we observed that outer segments formed in all Arl3 mutants.

4) Oddly, Arl3-Y90C does robustly bind Arl13 (Fig. 2C), while at the same time binding to effectors (Fig. 3D/E), although less strongly than the canonical Q71L constitutively active mutant (Fig. 2A). As noted in point #2, the Y90C/R149H double mutant, which fails to bind Arl13, abrogates the nuclear migration defect observed with Y90C alone. Although the authors refer to Y90C as "rapid cycling" its phenotype is more similar to a dominant-negative than an activated mutant.

We agree with this interpretation. We have now included language about Arl3-Y90C’s role as a dominant negative in that it blocks Arl13B activity. However, the rapid cycling behavior is important to cause the phenotype.

5) The authors also mention that loss of Arl3 has no phenotype in their assay, however, Arl3 knockout mice exhibit severe retinal degeneration. How do they explain this?

Our study finds that not all human Arl3 mutations will target the same cellular process even though they all result in degeneration. Arl3 knockout mice show drastic alterations in lipidated protein trafficking to the rod outer segment in mature retinas, a phenotype that we did not observe by expressing the dominant Arl3 mutants in wild type rods. Since our tools are not designed to study degeneration of rods, the precise mechanisms of degeneration caused by loss of function or dominant mutations remains to be determined. We outline some ideas in the discussion, but more work needs to be done before making any big statements regarding this. We hope that our manuscript will inspire clinicians to take a closer look at human patients to determine if there are subtle differences between disease presentation for dominant and recessive forms Arl3 inherited mutations. This is beyond the scope of our expertise.

Reviewer #3 (Public Review):

This work provides mechanistic insights into two recently described dominant variants of Arl3, a small GTPase, namely mutations D67V and Y90C. The authors identified a phenotype of these dominant variants during the development of rod photoreceptors by in vivo experiments in mice. They specifically observed a defect in rod nuclear migration to their final outer nuclear layer. This phenotype has been previously observed in another constitutively active variant of Arl3, Q71L. The authors performed a series of extensive and thorough biochemical assays to clarify the mode of action of these variants, mostly the Y90C variant, comparing the behavior of these variants to previously described mutants and combining multiple variants by mutagenesis. They also developed a new in vivo crosslinking strategy to be able to identify transient states of protein-protein interactions. They finally performed phenotypic rescue experiments by co-expression of various relevant proteins interacting/involved with Arl3. They finally propose a model based on differential subcellular compartmentalization of Arl3 activation which when disrupted leads to rod nuclei misplacement. These data add to the current understanding of contribution of different Arl3 variants causing human retinal degeneration, which has strong potential translational implications.

Strengths:

Relevance of Arl3 dominant variants to human retinal degeneration. Identification of Y90C variant as a "fast cycling" GTPase, and not as a predicted destabilizer of the protein structure.

New method of crosslinking to enable snapshots of endogenous protein-protein interactions.

Weaknesses:

• The relevance of this study is justified by the fact that newly identified dominant variants of Arl3 have been associated to retinal degeneration. However, the authors never assess a degeneration phenotype.

Electroporation technique allows for rapid expression of constructs, but the sparse expression makes it a poor means to study retinal degeneration. This is important to examine in the future using robust genetic mouse models.

• The authors show new dominant variants of Arl3, namely Y90C and D67V, cause rod nuclear mislocalization. This phenotype is interesting but this was previously observed with other constitutively active mutation of Arl3, Q71L, and therefore is not novel.

Yes, the Q71L paper is well cited in our manuscript and set the basis for many of our experiments.

• The main claim of this paper is that subcellular compartmentalization of Alr3 activation to the cilium (the so called gradient by the authors) is required for proper rod nuclear migration to their final outer nuclear layer destination. The authors provide multiple experiments to support this model, but this is never directly demonstrated.

We are not aware of any methods that could be done to directly show the subcellular localization of active Arl3-GTP within rod photoreceptors. We agree that we have provided many experiments that support our hypothesis that altering the Arl3-GTP gradient between cilium and cell body produces a nuclear migration defect. Some of our favorites include Fig 6, where we find that the migration phenotype is only rescued with expression of ciliary cargos and not rescued by non-ciliary cargos. Also, the new data requested by reviewers showing Arl13B expression in the cilium can restore the Y90C defect further supports that the Arl3 ciliary gradient is necessary for proper nuclear migration.

Author Response

Reviewer #1 (Public Review):

Pan et al. examined the role of oligodendroglial exocytosis, and specifically the role of L-type prostaglandin D synthase (LPGDS), in modulating oligodendrocyte differentiation and myelination. The topic of autocrine and paracrine signaling within the oligodendrocyte lineage is under-studied and the authors use a novel approach for oligodendrocyte precursor-specific inhibition of VAMP-mediated exocytosis using inducible expression of botulinum toxin with the PDGRFa-CreER transgenic mouse line (PD:ibot). Using a combination of in vitro culture systems and immunohistological analysis in vivo, the authors find ibot expression in OPCs leads to reduced oligodendrogenesis and myelination, leading to a behavioral deficit in rotarod performance. Additional transcriptomic analysis in PD:ibot mice revealed Ptgds, the gene encoding LPGDS, was significantly overexpressed in both mature oligodendrocytes and OPCs. Further pharmacological experiments with cultured OPCs showed direct LPGDS inhibition led to a similar inhibition of oligodendrogenesis as PD:ibot mice. Together, this study reveals VAMP-mediated exocytosis in OPCs is required for normal oligodendrogenesis and identifies LPGDS as a new chemical regulator of oligodendrocyte myelination. These findings are strengthened by careful characterization of the PD:ibot mouse line and effective use of culture systems and pharmacology to uncover a cellular mechanism. Quantification is performed at several levels of resolution using immunohistochemistry, electron micrography, and protein/transcriptomic analyses and control experiments were largely carefully considered.

We thank the reviewer for recognizing the strength of our study.

Despite these strengths, there are some points that need to be further addressed. The interpretation of autocrine/paracrine signaling relies on a critical culture experiment in which PD:ibot OPCs were cultured in the presence of PD:ibot or control OPC well inserts. However, these results had a marginal effect size, raising questions as to the extent to which VAMP inhibition specifically had effects through the blockade of exocytosis (resulting in an autocrine/paracrine signaling deficit) or inhibited oligodendrogenesis in a cell-intrinsic mechanism (e.g. VAMP-dependent trafficking of critical myelination components, such as PLP (Feldmann et al., 2011)).

We agree with the reviewer that both cell autonomous and cell non-autonomous effects may contribute to the defect associated with VAMP inhibition. We performed additional experiments to investigate the contribution of cell non-autonomous mechanisms. We took advantage of the fact that all OPCs purified from PD:ibot mice were not botulinum-GFP-expressing (efficiency ~65% Figure 6B, page 24). The GFP- cells in PD:ibot OPC cultures did not express botulinum toxin and were competent in exocytosis. We compared the development of GFP- control cells in cultures generated from PD:ibot mice vs. control cells in cultures generated from control mice. Interestingly, we found that the percentages and sizes of lamellar cells in control cells in PD:ibot cultures were smaller than in control cells in control cultures (Figure 6C, D text page 25). Although both groups of cells were competent in exocytosis, they were surrounded by exocytosis-deficient vs. exocytosis-competent neighbor cells. The differences in the growth capacity of control cells in the presence of different neighbor cells reveal cell non-autonomous contributions of botulinum-expressing cells in oligodendrocyte development.

As described above under Essential Revisions 4), we performed additional experiments on the role of the secreted protein L-PGDS in oligodendrocyte development. We found that adding a protein that inactivates PGD2, HPGD extracellularly to oligodendrocyte cultures inhibited their development (Figure 7F, G, page 33). Adding L-PGDS protein extracellularly to PD:ibot oligodendrocyte cultures rescued their development defect (Figure 9A, B, page 33). Moreover, overexpressing Ptgds in PD:ibot mice partially rescued the myelination defect (Figure 9E-H, page 36). These observations further strengthened our conclusion that cell non-autonomous mechanisms contribute to the effect of botulinum toxin on oligodendrocyte and myelin development.

Nevertheless, these results do not rule out the cell autonomous effect of botulinum on oligodendrocyte development and, therefore, we included the potential contribution of both cell autonomous and cell non-autonomous mechanisms in the text.

Additionally, the authors claim the reduced number of oligodendrocytes in PD:ibot mice in vivo is not due to oligodendrocyte apoptosis and provide evidence by cleaved caspase-3 immunostaining of the cerebral cortex. While statistically not significant, the data is highly variable.

We thank the reviewer for pointing out the variability of the caspase-3 results. We performed a more thorough analysis of activated caspase-3 at multiple developmental stages. Again, we did not find any statistically significant difference in apoptosis between PD:ibot and control oligodendrocytes, OPCs, or cells of other lineages (Figure 3-figure supplement 1, text page 13).

If true, this would suggest oligodendrocyte differentiation is inhibited, which would coincide with a reduction of OPC proliferation. A complementary experiment comparing the rates of OPC proliferation between control and PD:ibot mice in vivo would provide further clarity on how oligodendrocyte density is being reduced.

We analyzed OPC proliferation in vivo by staining and quantifying Ki67+PDGFRa+ cells. Intriguingly, we found a modest increase in OPC proliferation in PD:ibot mice (Figure 3-figure supplement 3, text page 14).

The relevance of these myelination deficits is assessed with a rotarod assay, however, the mice used for these experiments are several times older (2-5 months) than those used for all other histological quantification (P8-P30). The large variance in results could be due to age-related differences in myelination, and it is unclear whether the deficits at early timepoints show a linear progression with age.

We thank the reviewer for the insightful comment. We have separately labeled data points from 2 months old and 5 months old mice (Figure 3Q-S, text page 17). With the data we have so far (n=20-27 per genotype), there isn’t a striking progression of phenotype with age. Future analysis at multiple time points may resolve any age-dependent changes in the phenotype.

Reviewer #3 (Public Review):

The authors pose an important question of whether oligodendrocyte lineage cells have an autocrine/paracrine signaling loop that contributes to their differentiation and myelination. While prior studies have demonstrated oligodendrocyte lineage cells have cell-intrinsic pathways that impact differentiation and myelination, there isn't a strong precedent for oligodendrocytes to promote their own differentiation via autocrine/paracrine mechanisms. The notion that oligodendrocyte lineage cells promote their own differentiation in an autocrine/paracrine manner is an intriguing one that adds a new layer to our understanding of how oligodendrocyte maturation is controlled. I anticipate this paper will prompt a new direction of future investigations to uncover the extent of oligodendrocyte autocrine/paracrine signaling.

To test the possible role of oligodendrocyte-secreted molecules on oligodendrocyte development, Pan et al. utilized a mouse model where the release of a subset of secretory vesicles (specifically VAMP1/2/3-dependent vesicles) is blocked. Blocking this vesicular release prevented or delayed the differentiation of oligodendrocytes in vivo and in vitro. Further, the authors identified changes to the mRNA and secreted protein levels of prostaglandin D2 synthase (L-PGDS). Prior RNA sequencing and snRNA sequencing datasets of the oligodendrocyte lineage have identified Ptgds as a highly abundant mRNA transcript in oligodendrocyte lineage cells, particularly mature oligodendrocytes. Ptgds encodes L-PGDS, which has an unknown role in oligodendrocyte function. L-PGDS has been shown to regulate Schwann cell myelin formation in the peripheral nervous system, prompting the question of whether this protein acts similarly in the central nervous system. The paper has a clear set of well-rounded experiments, with a few remaining points that would strengthen the conclusions:

We thank the reviewer for the positive comments on our study.

One of the foundational conclusions of the study is that VAMP1/2/3-dependent exocytosis is critical to oligodendrocyte maturation, by using a PDGFRa-CreER mouse line combined with iBot mice that express botulinum toxin in Cre-expressing cells (abbreviated as PD:iBot). Prior work has demonstrated in vitro that oligodendrocyte morphological maturation, myelin gene expression and myelin protein transport can all be impacted by the loss of VAMPs, including VAMP3. This paper establishes the importance of these SNARE proteins in the oligodendrocyte lineage in vivo: the number of mature (CC1+) oligodendrocytes and myelin basic protein staining is substantially reduced in PD:iBot mice.

1) The data in Figure 3M suggests that PD:iBot oligodendrocytes (GFP+) are lacking MBP+ sheaths and that any myelin formed is by the smaller percent of oligodendrocytes that do not express botulinum (GFP- cells). Furthermore, the efficiency of iBot expression (as evaluated by GFP+ cells) shows that 80% of OPCs and just 60% of oligodendrocyte lineage cells express GFP at P8 and supplementary data shows just 30% of oligodendrocyte lineage cells express GFP at P30. This raises the question of whether PD:iBot cells are unable to differentiate and die. While the authors show no change in caspase-dependent apoptosis in PD:iBot cells in vivo and in vitro, the data still suggests that blocking VAMP-dependent exocytosis itself slows or prevents the progression to a fully myelinating oligodendrocyte in vivo rather than the putative autocrine/paracrine signals are required for OPC differentiation. Confirming whether botulinum-expressing cells also contribute to the population of surviving, differentiated oligodendrocytes in vivo to strengthen the conclusions that autocrine/paracrine secreted molecules contribute to the oligodendrocyte maturation in vivo.

We thank the reviewers for raising a key point in characterizing the consequence of botulinum toxin expression in oligodendrocyte-lineage cells. We analyzed the overlap between GFP+ botulinum-expressing cells and the population of differentiated oligodendrocytes (Olig2+PDGFRa-CC1+ cells) and found that botulinum-expressing cells can survive and become differentiated oligodendrocytes (Figure 3-figure supplement 2, text page 14). Additionally, we performed a more thorough analysis of activated caspase-3+ apoptotic cells than was included in first submission and did not detect statistically significant differences between PD:ibot and control mice (Figure 3-figure supplement 1, text page 13).

2) The paper has complementary in vitro data to pinpoint a mechanism that results in hindered oligodendrocyte maturation. The authors conduct a well-designed set of in vitro co-culture experiments in Fig4 K-M that led them to conclude oligodendrocyte morphology is impacted by secreted molecules from other oligodendrocytes.

2a) The key experiment is the transwell co-culture experiment with control and iBot cells, which suggests that blocking secretion itself has the predominant impact on cell morphology: by eye, both group3 and 4 show the largest reduction in lamellar area and the difference between group 3 and 4 is slight. At day 3 of culture (Fig 4E), the authors show the clearest effect as a reduction in cells with lamellar morphology. The quantification of the lamellar cell area is less obvious than the % of cells with arborized vs lamellar shape, as seen in Figures E & F. I would recommend that the authors show representative images of these observations and quantification of morphologies for the transwell experiments. The impact of secreted factors may be clearer with this measure.

We added representative images (Figure 6G). We quantified both the % and size of lamellar cells. The size of lamellar cells is significantly higher in group 4 than in group 3. Although the % of lamellar cells is numerically higher in group 4 than in group 3, the difference is not statistically significant. To further assess whether cell non-autonomous mechanisms contribute to the oligodendrocyte development defect in PD:ibot mice, we performed additional analysis in culture. We took advantage of the fact that all OPCs purified from PD:ibot mice were not botulinum-GFP-expressing (efficiency ~65% Figure 6B). The GFP- cells in PD:ibot OPC cultures did not express botulinum toxin and were competent in exocytosis. We compared the development of GFP- control cells in cultures generated from PD:ibot mice vs. control cells in cultures generated from control mice. Interestingly, we found that the percentages and sizes of lamellar cells in control cells in PD:ibot cultures is smaller than in control cells in control cultures (Figure 6C, D, text page 25). Although both groups of cells were competent in exocytosis, they were surrounded by exocytosis-deficient vs. exocytosis-competent neighbor cells. The differences in the growth capacity of control cells in the presence of different neighbor cells reveal cell non-autonomous contributions of botulinum-expressing cells in oligodendrocyte development.

2b) On a related note, the cell morphology data is dependent on MBP staining. The authors show that MBP protein is reduced in cells from iBot mice. Since MBP+ cell area/arborized or lamellar structure is being quantified, there remains the possibility that the cells could display a more complex morphology (lamellar) that may be missed by only staining for MBP. The authors use a CellMask dye to show cellular morphology, which is a great idea. The authors state that it labels the plasma membrane; however, the methods (and images) indicate that a cytoplasmic CellMask was used (cat.no. H32720 labels nuclei and cytoplasm, not membranes). These conclusions about cell morphology vs simply MBP expression would be strengthened by an alternative membrane label (e.g., a CellMask plasma membrane dye).

We thank the reviewers for the insightful suggestion. We used the membrane version of CellMask and repeated the transwell co-culture experiment. The new results are consistent with the results based on MBP (Figure 6-figure supplement 1, text page 23). In addition, we used the membrane version of CellMask for all the new cell culture experiments (L-PGDS rescue, HPGD etc.)

3) The authors sought to identify what secreted factors may be affected by blocking VAMP1/2/3-dependent exocytosis. Pan et al. opted for a strategy of examining transcriptional changes, asserting that important genes may be upregulated in response to compensate for blocked secretion. While this is an indirect way to identify secreted candidates, the authors found a fortuitous result that Ptgds was substantially increased in the PD:iBot oligodendrocyte cells. To confirm that L-PGDS secretion is reduced from iBot cells, the authors show Western blots. By eye the change in L-PGDS is variable, however, the authors conduct several experiments with an inhibitor and product of L-PGDS that nonetheless indicate L-PGDS activity can contribute to the morphological maturation of oligodendrocytes. A caveat is that the AT-56 inhibitor reduces MBP+ cells, and the quantification of morphology is dependent on MBP staining (again, see my note in 2b about the CellMask dye). A report on differentiation (% MBP+ cells) may be a more accurate reflection of the result.

We repeated the AT-56 experiment using the membrane version of CellMask and again found that AT-56 inhibits oligodendrocyte maturation (Figure 7-figure supplement 2, text page 33).

The key, compelling experiment demonstrating the role of prostaglandin D2 is the authors' rescue experiment in Fig 4G.

As described above under Essential Revisions 4), we performed additional rescue experiments on the role of L-PGDS in oligodendrocyte development. We found that adding L-PGDS protein extracellularly to PD:ibot oligodendrocyte cultures rescued their development defect (Figure 9A, B, page 34). Moreover, overexpressing Ptgds in PD:ibot mice partially rescued the myelination defect (Figure 9E-H, page 36).

4) Although it's not a direct demonstration that L-PDGS secretion from oligodendrocytes is the key factor, the global L-PDGS knockout mice phenocopy many of the observations of the PD:iBot mice. This is a nice set of observations consistent with the author's hypothesis that L-PDGS impacts oligodendrocyte maturation. Future work should pinpoint whether oligodendrocyte-derived L-PDGS is critical.

We agree with the reviewer that pinpointing whether oligodendrocyte-derived L-PGDS promotes oligodendrocyte development and myelination is an interesting direction to pursue in future work. We are breeding L-PGDS conditional knockout mice to address this question and may report the results in a separate paper in the future.

Minor points:

1) The authors demonstrate that PD:iBot expresses botulinum and loses VAMP2 protein levels in oligodendrocyte lineage cells, but there is no demonstration of whether VAMP3 is expressed or similarly affected. Prior work has demonstrated in vitro that oligodendrocytes express both VAMP2 and VAMP3 (VAMP1 not detected). This would more clearly demonstrate which VAMP-mediated vesicular transport is blocked for the effects observed.

We agree with the reviewer and examined VAMP3 levels with Western blot. We found diminished levels of VAMP3 in oligodendrocyte-lineage cells from PD:ibot mice (Figure 1 J, M, text page 10).

2) It is satisfying to observe a behavioral effect in the PD:iBot mice. I would advise caution in interpreting any direct link between oligodendrocytes maturation and the rotarod behavioral difference at this time. Blocking secretion from PDGFRa-Cre expressing cells may have many indirect effects (beyond myelination) in both the CNS and other cell types that can express PDGFRa and VAMPs1/2/3. I was pleased that the authors did not conclude any direct links at this time.

We agree with the reviewer.

Overall, the authors had a well-rounded manuscript with clearly described and thoughtful experiments. The data support the conclusion that VAMP-mediated exocytosis is critical for oligodendrocyte maturation. The evidence that reduced L-PDGS secretion from the oligodendrocytes can explain the effects of the iBot mice is not as clear cut, but their data does demonstrate that L-PDGS is an important molecule for the differentiation of oligodendrocytes. This work will lead a new direction for future studies to investigate autocrine/paracrine signaling in oligodendrocyte maturation.

We thank the reviewer for the positive comments on our manuscript. As detailed in Essential Revisions 4), we now provide additional evidence on the potential contribution of L-PGDS in the oligodendrocyte development defect in PD:ibot mice.

Author Response

Reviewer #3 (Public Review):

Garratt et al. investigated that transient exposure of young mice during their first two months of life with olfactory cues from con-specific adults would have long-lasting effects on their late-life health and lifespan. They find that the olfactory cues have sex-specific effects on lifespan, which only the lifespan of young females can be extended by odours from adult females but no other combinations, neither young females with adult males nor young males with either sex. Interestingly, their data also suggested that depletion of G protein Gαo in the olfactory system played no role in the lifespan extension, indicating it might be another unknown factor(s) mediating this sex-specific effect on longevity in mice. While the conclusions of this study are well supported by the data, there are some issues with parts of the data analysis and presentation that would need to be clarified and extended.

1) The authors suggested that the G protein Gαo played no role in lifespan extension in the case that transient exposure of young females with olfactory cues from female adults, as they showed in Figure 1. However, it is not clear if the depletion of G Gαo (Gαo mutant) itself has effects on lifespan, compared to its wild type. It would be important to show the lifespan curves from wild type and Gαo mutant individually alongside the pooled lifespan curves, as well as regarding data in a table, followed with a proper discussion.

Data for genotypes is now shown individually.

2) Regarding the functional tests, the authors showed that there was only a small fraction of experiments showed differences between treatments, which were all in figure 2. However, it is necessary to also show the data with no differences, particularly since the conclusion of the study suggested the underlying mechanisms are not clear yet. In my opinion, body weight, plasma glucose, and body temperature all deserve to have their figures individually with all data points.

This data is now shown.

3) As the authors mentioned in the Introduction, the age at sexual maturity correlates positively with the median lifespan across mice strains (Yuan et al. 2012, Wang et al. 2018). Also, young female mice that were exposed to male odours during their developmental stage accelerated sexual maturity (Drickamer 1983), and the same happened to young males that were exposed to the odours from the opposite sex (Vandenbergh 1971). It is, therefore, surprising to see in this study, the exposure of young females or young males to the olfactory information from their opposite sex had no effects on lifespan. One of the solutions to solve this disparity is to measure the sexual maturity of the mice in this study. The authors should seek the possibility to check the record of when the first litter of pups was born between treatments (Shindyapina et al. 2022) or examine preputial separation and vaginal opening (Hoffmann 2018), for instance.

The animals used in the lifespan experiment were not allowed to breed so as not to interfere with the lifespan assessment. Similarly, we did not check animals within the lifespan experiment for sexual maturity as we wanted to minimize the handling of animals after weaning, and this requires daily handling and/or vaginal swabbing.

We conducted a preliminary experiment prior to the main lifespan experiment (in UM-Het3 mice) to test whether sexual maturity was modulated in the expected directions with the odour exposure protocol we planned to impose. This experiment showed that the odor manipulation we applied has the expected effects on sexual maturity. We have now outlined this experiment and its results in the methods section of the paper to justify the odor treatment protocol.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the author characterizes the lattice of kinesin-decorated microtubule reconstituted from porcine tubulins in vitro and Xenopus egg extract using cryo-electron tomography and subtomogram averaging. Using the SSTA, they looked at the transition in the lattice of individual microtubules. The authors found that the lattice is not always uniform but contains transitions of different types of lattices. The finding is quite interesting and probably will lead to more investigation of the microtubule lattice inside the cells later on for this kind of lattice transition.

The manuscript is easy to read and well-organized. The supporting data is very well prepared.

Overall, it seems the conclusion of the author is justified. However, the manuscript appears to show a lack of data. Only 4 tomograms are done for the porcine microtubules. Increasing the data number would make the manuscript statistically convincing.

One tomogram can contain one to several tens of microtubules. For example, 64 microtubules were analyzed in the Xenopus-DMSO dataset obtained on 5 tomograms, versus 24 microtubules for the GTP-dataset obtained on 4 tomograms (see Table 1). Hence, taking the number of tomograms to assess the statistical relevance of our work cannot be considered as a valid criterion. Tomograms are taken randomly on the EM-grid sample, solely based on ice quality and the covering of microtubules in the holes as determined at low magnification before tomographic acquisition. No prior knowledge of the structure and lattice-type organization of the microtubules can be obtained before acquisition. It appears to us that a more pertinent criterion is the number of events that we characterized, specifically lattice-type transitions along individual microtubules. In the dataset mentioned by the referee (see Figure 2-figure supplement 3-4 and Table I), 24 microtubules were analyzed and further divided into 195 segments, providing an equivalent number of individual 3D reconstructions. For each 3D reconstruction, almost all lateral interactions could be characterized in terms of lattice-type, i.e., 2091 of the B-type, 460 of the A-type, and 112 not determined (essentially at transition regions). Most importantly, we document in this specific dataset 119 transitions in lattice-type, which we think is sufficient to characterize such molecular events and provide solid statistics for this dataset. Adding the GMPCPP and Xenopus data, we end-up with 938 individual 3D reconstructions (not including the full-length microtubule volumes), 12 463 lateral interactions analyzed (A-, B-, or ND-type), and the observation of 172 lattice-type transitions. Therefore, we respectfully disagree with the referee stating that our work lacks data.

To highlight the quantity of data used in our work, we have modified the following sentences: L124-131: ' Analysis of 24 microtubules taken on 4 tomograms, representing 195 segments of ~160 nm length (i.e., 2664 lateral interactions), allowed us to characterize 119 lattice type transitions with an average frequency of 3.69 µm-1 (Table 1), but with a high heterogeneity' L160-164: ' Analysis of 31 GMPCPP-microtubules taken on 6 tomograms, representing 338 segments of ~150 nm in length (i.e., 3236 lateral interactions), and using the same strategy as in the presence of GTP (Figure 5—figure supplement 1-2) revealed a transition frequency of 1.25 µm-1 (Table 1), i.e., ~3 fold lower than microtubules assembled in the presence of GTP.' L200-203: ' A total of 64 microtubules taken on 5 tomograms were analyzed in the Xenopus-DMSO dataset (i.e., 419 segments from which we characterized 5446 lateral interactions), and 15 microtubules taken on one tomogram for the Xenopus Ran-dataset (i.e., 86 segments from which we characterized 1118 lateral interactions), (Table 1).'

In addition, having the same transition with the missing wedge orientation randomly from different subtomograms will allow a better average of transition without the missing wedge artifact.

In this work, we did not aim at averaging transitions. Transitions in lattice-types are highly heterogeneous in nature, and we wonder what additional information an averaging strategy would have provided. Conversely, each transition is a unique event that we characterized to obtain useful statistics, and the missing data at high angle inherent to electron tomography were not an obstacle to fulfill this task.

Another thing that I found lacking is the mapping of the transition region/alignment in the raw data.

In Figure 4, we clearly show the correspondence between the segmented sub-tomogram averages (SSTA) and the raw filtered images at the transition region. This is also the case in Figure 5 where the SSTA (Figure 5A) are compared with the raw tomogram (Figure 5B), and where we clearly visualize the holes that result from the transitions in lattice types.

However, it is not easy for me or the reader to understand how each segment is oriented relative to each other apart from the simplified seam diagrams in the figures, and also the orientation of the seam corresponding to the missing wedge in the average. With these improvements, I think the conclusion of the manuscript will be better justified.

The segmentation process is explained in Figure 2-figure supplement 2 and in the Materials and Methods section, which shows that each segment is linearly related to the next. Small rotations can happen between individual segments, and it is important to check that the same protofilaments are followed during the initial modeling (see the online tutorial referenced in the manuscript for full-length microtubules). The segment models are derived from that of the full-length microtubule, as explained in the Materials and Methods section, using a new routine (splitIntoNsegments) implemented into the PEET program. In addition, a detailed protocol describing our SSTA strategy will be submitted following publication of our manuscript.

Reviewer #2 (Public Review):

Differences in protofilament and subunit helical-start numbers for in vitro polymerized and cellular microtubules have previously been well characterized. In this work, Guyomar et al. analyze the fine organization of tubulin dimers within the microtubule lattice using cryo-electron tomography and subtomogram averaging. Microtubules were assembled in vitro or within Xenopus egg cytoplasmic extracts and plunge frozen after addition of a kinesin motor domain to mark the position of tubulin dimers. By generating subtomogram averages of consecutive sections of each microtubule and manually annotating their lattice geometry, the authors quantified changes in lattice arrangement in individual microtubules. They found in vitro polymerized microtubules often contained multiple seams and lattice-type changes. In contrast, microtubules polymerized in the cytoplasmic extract more frequently contained a single seam and fewer lattice-type transitions.

Overall, their segmented subtomogram averaging approach is appropriately used to identify regions of lattice-type transition and quantify their abundance. This study provides new data on how often small holes in the lattice occur and suggests that regulators of microtubule growth in cells also control lateral tubulin interactions. However, not all of the claims are well supported by their data and the presentation of their main conclusions could be improved.

1 - We have corrected approximative claims and conclusions where necessary. In particular, we now discuss separately the Xenopus-DMSO and the Xenopus-Ran egg extract samples, and have modified our conclusions accordingly. We also deposited onto the EMPIAR all tomograms and PEET models to reproduce the 938 segmented sub-tomogram averages analyzed in this study (see new Supplementary file 2).

Reviewer #3 (Public Review):

Protofilament number changes have been observed in in vitro assembled microtubules. This study by Guyomar and colleagues uses cryo-ET and subtomogram averaging to investigate the structural plasticity of microtubules assembled in vitro from purified porcine brain tubulin at high concentrations and from Xenopus egg extracts in which polymerization was initiated either by addition of DMSO or by adding a constitutively active Ran. They show that the microtubule lattice is plastic with frequent protofilament changes and contains multiple seams. A model is proposed for microtubule polymerization whereby these lattice discontinuities/defects are introduced due to the addition of tubulin dimers through lateral contacts between alpha and beta tubulin, thus creating gaps in the lattice and shifting the seam. The study clearly shows quantitatively the lattice changes in two separate conditions of assembling microtubules. The high frequency of defects they observe under their microtubule assembly conditions is much higher than what has been observed in vivo in intact cells. Their observations are clear and supported by the data, but it is not at all clear how generalizable they are and whether the defect frequencies they see are not a result of the assembly conditions, dilutions used and presence of kinesin with which the lattice is decorated. The study definitely has implications for mechanistic studies of microtubules in vitro and raises the question of how these defects vary for protocols from different labs and between different tubulin preparations.

1 - High tubulin concentration: It has been documented by many laboratories since the discovery of tubulin and the characterization of its assembly properties that a sufficient concentration of free tubulin is necessary to self-assemble microtubules. This is called the critical concentration for self-assembly (the CC, i.e., the critical concentration to overcome the nucleation barrier), and has been reported to be in the range 14~25 µM in the presence of GTP depending on laboratories. For example, in the seminal work of Mitchison and Kirschner the CC was estimated at 14 µM (Fig. 5 of ref. (Mitchison & Kirschner, 1984b)) and self-assembly was induced at concentrations in the range 32-59 µM (Mitchison & Kirschner, 1984a). Our own estimate of the CC for porcine brain tubulin was 21 µM (Fig 2C of (Weis et al., 2010)), and we routinely use a tubulin concentration slightly above the CC when we aim at robust microtubule self-assembly. Hence, we argue that 40 µM, which is ~twice the CC, cannot be considered as a "very high" tubulin concentration to induce microtubule self-assembly.

2 - Protofilament number and lattice-type transitions in cells: While microtubules with protofilament numbers different than 13 have been observed in different cell types and species (reviewed in (Chaaban & Brouhard, 2017)), we are aware of only one recent study where changes in protofilament numbers along individual microtubules have been reported in cells (Foster et al., 2021), but with no statistics concerning their frequencies. Hence, we cannot compare changes in protofilament number frequencies in Xenopus egg extracts with those that occur in intact cells. Concerning lattice-type transitions, we are not aware of any previous study that documented such features, whether in vitro or in cells.

3 - Generalization of our results, source of tubulin and protocols: Multi-seams in microtubules assembled in vitro have been reported by several groups in the past (see our Introduction, L49-62), starting from (Kikkawa et al., 1994), the Milligan group (Dias & Milligan, 1999; Sosa et al., 1997), and more recently by the Sindelar group (Debs et al., 2020). In Kikkawa et al. (1994), the authors purified tubulin from porcine brain by three cycles of assembly/disassembly followed by phosphocellulose chromatography. Assembly was carried out at 24 µM in the presence of Taxol. In Sosa and Milligan (1996-1997), the authors used a commercial source (Cytoskeleton) and assembled the microtubules at 30 µM in the presence of Taxol. In Debs et al. (2020), the authors used tubulin purified from porcine brain according to (Castoldi & Popov, 2003), as we did, to assemble GMPCPP microtubules, and bovine brain tubulin (Cytoskeleton) to assemble Taxol-stabilized microtubules. Noticeably, they used an initial tubulin concentration of 100 µM to initiate microtubule polymerization and then added Taxol to continue the reaction.

We add to these previous studies that microtubules with different numbers of seams are not unique ones, but that both the number and location of seams can vary within individual microtubules. The reason why this was not observed before is that the analytical tools used in those previous studies were not suited to reveal this structural heterogeneity within individual microtubules. By contrast, the SSTA approach that we designed was specifically developed towards this aim. Even in the recent work by Debs et al. (2020) that provides the most comprehensive characterization of multi-seams in microtubules assembled in vitro and that obtained a seam distribution very similar to ours (compare their Figure 3C with our new Figure 10C for GDP microtubules, dark blue bars), their protofilament-based approach could not reveal changes in the number and location of seams within individual microtubules. Yet, they probably could have done it if they had asked whether segments with different seam numbers had been extracted from the same microtubules.

Here, we designed a specific approach to tackle the structural heterogeneity of individual lattices that permitted this discovery. Not only do we confirm results obtained by others, but we also propose a molecular mechanism that explains how multi-seams form in microtubules assembled in vitro and how they change in location in a cytoplasmic environment. By doing so, we propose a novel molecular event - formation of unique lateral interactions without longitudinal ones - that was not envisioned before, and which to our opinion, must be incorporated in further modelling studies concerning microtubule nucleation and assembly, including the mechanism of dynamic instability (see the Ideas and speculation section).

4 - Dilution: A 50X dilution was used only for Xenopus egg cytoplasmic extracts to decrease their density on the EM grid just before freezing. These conditions were settled by cryo-fluorescence microscopy to ensure that we had the adequate density of microtubules onto the EM-grid (Figure 7 and Figure 2—figure supplement 1D). Of note, the microtubules analyzed by SSTA were assembled in extracts that were not supplemented with fluorescent tubulin. While we could imagine that dilution may induce the removal of dimers from the microtubule lattice, we cannot foresee how this could change the register between tubulin subunits within the microtubule lattice.

5 - Kinesin decoration: Like many other laboratories (see the Table in Figure 3 of (Manka & Moores, 2018)), we use the non-processive motor domain of kinesin 1 to decorate microtubules, with the aim to differentiate the - and -tubulin monomers within the microtubule lattice. In particular, it has been shown that lattice parameters such as the protofilament skew and lattice spacing are unmodified when kinesin motor domains are added to GMPCPP- or GDP-microtubules (Zhang et al., 2015, 2018). In addition, we cannot envisage how this non processive motor added to preformed microtubules could change the registry of the -tubulin heterodimers within the microtubule lattice.

Author Response

.Reviewer #1 (Public Review):

1) It is important to emphasize that the osteoporotic phenotypes were only demonstrated in males, but not in female mice. The observed phenotypes were not hormone-dependent, as no significant differences in examined bone parameters were observed between wild type andPrdx5KO female mice in an ovariectomy-induced osteoporosis model. However, women over 50 have a four times higher rate of osteoporosis compared with men, and the role of testosterone in the development of osteoporosis in Prdx5KO mice should be investigated. It is known that the osteoporosis is increased in men with low level of testosterone.

Thanks for your comments regarding osteoporosis phenotypes in Prdx5 KO males and their relation with testosterone levels. Based on your suggestion, we re-examined testosterone levels in the serum of male mice and tested the expression levels of the androgen receptor (AR) in the differentiated osteoblasts and osteoclasts of the mice. We have updated the data in Figure 3-figure supplement 2 and included the revised information in the Results (Pages 13-14) and Discussion (Page 34) sections.

2) It is misleading for authors to state throughout the manuscript that osteoporotic phenotypes are observed in Prdx5KO mice, while it is only observed in male mice.

We apologize for this oversight. We have modified the text and indicated that all osteoporotic phenotypes were observed in Prdx5 KO male mice.

Reviewer #2 (Public Review):

1) While the abstract emphasizes transcriptomic analysis and mass spectrometry, extensive imaging techniques have also been used and should be highlighted to give an overview of results from the performed techniques.

In addition, make it clear that it is proteomics-based mass spectrometry, since I was only able to confirm that after seeing Figure 5.

Thanks for your helpful suggestions. We have modified the Abstract based on your suggestions.

2) Line 46-53: I would add more details of how balanced bone mass looks on average, how much is too much, when should we be concerned about bone mass, and does some amount of stress benefit bone mass?

Thank you for the suggestion. We have modified the Introduction. We wanted to explain that for bone as a supporting organ, general mechanical stress is required for its remodeling, although we agree that it is not some necessary information related to our study and may confuse the readers.

Author Response

Reviewer #3 (Public Review):

Results of this manuscript provide a new link between oxygen sensing and cholesterol synthesis. In previous studies, this group showed that the cholesterol synthetic enzyme squalene monooxygenase (SM) is subjected to partial proteasomal degradation, which leads to the production of a truncated, constitutively active enzyme. In this study, the authors provide evidence for the physiological significance of SM truncation. In a series of experiments, the authors show that subjecting cells to hypoxia (oxygen deprivation) induces truncation of SM. The synthesis of cholesterol requires 11 molecules of oxygen and SM is the first oxygen-dependent enzyme in the cholesterol-committed branch of the pathway. Evidence is presented that hypoxia causes squalene, the substrate of SM, to accumulate, which results in the enzyme's truncation. In addition, hypoxia stabilizes MARCHF6, the E3 ligase required for sterol-dependent ubiquitination and degradation of SM. Finally, the authors provide an experiment showing that truncation of SM correlates with hypoxia in endometrial cancer tissues.

Overall, the data presented in this manuscript are compelling for the most part. Hypoxia-induced truncation of SM and MARCHF6 is very clear according to the presented results. The specificity of SM-induced truncation is strong; both direct addition and inhibitor studies are presented. The major strength of this manuscript is that it provides the physiological relevance for the authors' previous finding that squalene accumulation leads to truncation of SM. However, there are a few issues that should be addressed to improve the interpretation of the data presented.

We thank the reviewer for their useful comments.

The manner in which quantified immunoblots are presented is very confusing and difficult to interpret. This is evident in experiments in several figures. For example, it is difficult to determine the role of ubiquitination (Figure 2D) and MARCHF6 (Figure 2E) in the generation of truncated SM. The authors should present quantified data of all lanes of the immunoblots to reduce confusion.

The revised manuscript includes quantification of protein levels for all immunoblot lanes, including in Figure 2D and Figure 2E (now Figure 3A). It also contains updates to the text, figure legends, and axis labels to improve clarity about data normalization. For more information, please refer to our response to Essential Revisions comment #1.

The other important finding of this manuscript is that hypoxia stabilizes MARCHF6. This is supported by the results of Fig. 3A; however, the result of Figure 3B is not clear. A new band appears upon inhibition of VCP and MG-132 seems to reduce protein expression. These results could be removed from the manuscript without impacting the conclusions drawn.

As suggested, the revised manuscript contains only the initial observation that hypoxia stabilizes MARCHF6. Other experiments investigating the mechanism have been removed. For more information, please refer to our response to Essential Revisions comment #2.

Finally, the results shown in Figure 5 showing that truncation of SM correlates with hypoxia in endometrial cancer tissues are a little preliminary. Multiple bands are detected in SM immunoblots, which interferes with interpretation. This experiment could be removed and speculated upon in the discussion.

As suggested, this experiment is removed from the revised manuscript.

Author Response

Reviewer #1 (Public Review):

They established a "behavioral transcriptomics" platform as they cultured mouse primary cell explant on an apparatus, imaged the cells over time, and analyzed cells with differential physiological status by scRNA-seq. They showed evidence that the system recapitulated physiological features of airway cells, including chemical-induced damage response. They further utilized the system to isolate cells of different cellular features and analyzed gene expression through scRNA-seq. The study demonstrates an interesting establishment and application of an in vitro system mimicking in vivo.

However, several major concerns need to be resolved.

First, whereas the overall study seems to focus on the establishment of airway epithelial cell explant apparatus and its application, take home messages that are delivered by the authors seem to emphasize the transcriptome analysis part. The authors introduced "spatial transcriptomics" and"behavioral transcriptomics" in the abstract but it is hard to appreciate that the study resolves spatial transcriptomics. This causes unnecessary confusion. Second, probably related to the first question, it is hard to find the novelty of the study. Third, probably the last and most important part of the manuscript is to analyze the cells by Smart-seq. But the analysis was performed on the SO2 injured animal only and lacked experiment on wildtype mice. If the authors tried to prove the feasibility of the technique rather than resolving physiological mechanism here, then I would recommend explaining why wild type experiment was not performed.

The method described in the manuscript consists of two components: a novel tissue imaging platform, and characterization of a cellular behavior. Both steps can be generalized to different tissue contexts and different cellular behaviors, respectively. We have revised the title and abstract to specify the scope of this study and have also revised the text accordingly.

Live imaging allows us to observe cell behaviors in intact tissues but does not provide information on cell type. By profiling cells that are observed by live imaging to share a behavior at single-cell resolution rather than bulk, we can separate out sources of transcriptional variation, like cell type identity, in order to identify the transcriptional signatures that reflect cell behaviors.

Single-cell sequencing (via Smart-seq) has been previously performed in wild-type mouse trachea (Montoro et al., 2018), and identified underlying cellular heterogeneity. However, the steady state tracheal epithelium is largely quiescent, characterized by slow turnover and a lack of visible cell motility. We performed daily imaging of trachea explants from uninjured mice over 4 days and did not observe any significant displacement of epithelial cells. Furthermore, we also imaged an uninjured explanted tracheal epithelium every 40 minutes for over 19 hours with no significant directional movement (new Movie 3). We added the following text to the manuscript: “Imaging of trachea explant controls from uninjured mice over 19 hours revealed no cellular displacement in the airway epithelium (Movie 3).”

In contrast, regeneration activates cell motility followed by cell proliferation. Therefore, we chose tissue regeneration as the more suitable biological context for this study to examine cellular dynamics. We leveraged the gene signatures derived from the previous wild-type study (Montoro et al., 2018) to identify different cell types and make like-for-like comparisons. We used an independent regeneration dataset in the same tissue but with a different injury model (Plasschaert et al., 2018) to test whether the molecular signatures derived in our study that differentiate moving and non-moving cells are generalizable to other contexts.

Reviewer #2 (Public Review):

Kwok et al. devise a method that uses a transgenic mouse line to make the link between cell behaviour in intact living tissue and subsequent dissociation into distinct groups forsingle cell sequencing. Specifically, they set up a mouse airway culture system in which it is possible to maintain live cells for multiple days and then preserve the same tissue. The analysed tissue section can be fixed and known cell types identified via classical staining protocols. In this system they imaged a number of tissue phenotypes such as ciliary beating, mucociliary clearing and airway regeneration. With respect to airway regeneration they observe that there was cellular heterogeneity between cells with the capacity to move and so-called non-movers, which the authors were able to quantitively track.To make the link with single cell sequencing, they use the Kaede transgenic mouse lines,which contains a green fluorescent reporter gene, that can be converted into a red fluorescent reported gene by illuminating a defined tissue section, in this case regions enriched for movers or non-movers. After dissociation of the tissue, cells were FACSsorted using the reporter protein. Subsequent single cell RNAseq revealed distinct gene signatures that were associated with the mover versus the non-mover phenotype. These phenotypes could also be detected in previously published data sets.

The conclusions of the paper are supported by the data that is presented, but the comparison to existing mouse injury data could be improved. A weakness of the paper is the implication that the technique can be used for any of the phenotypes that they have examined. However, in order to be assessed by this method,there need to be a reasonably large number of cells that show similar behaviour in a region that can be photoconverted. If it is indeed possible to do the photoconversion at the single cell level, the authors should demonstrate that such resolution is possible, or otherwise clearly state this limitation of the technique they have developed.

We recognize that the approach in this study does not involve photoconversion at single-cell resolution. While single-cell photoconversion and subsequent intermittent live imaging has been demonstrated in other systems such as zebrafish (Green and Smith, 2018) and mouse skin (Park et al., 2017), the throughput of doing downstream single-cell analysis would be limited, especially in a cell type-specific manner. Having observed a relatively homogeneous behavior of cells within a small region (~200 μm diameter, Movie 1 and Movie 2) of the airway epithelium, we photoconverted a small area with several hundred cells. Subsequent single cell sequencing allowed us to compare differences in gene expression between basal cells of slow/non-moving regions to basal cells of fast/moving regions.

Reviewer #3 (Public Review):

In this manuscript, the authors identify a pressing need to couple visualized in situ cell behaviour with deep molecular profiling of visualized cells, aiming to move beyond inferences made from time-lapse tissue sampling approaches or the analysis of transcriptional kinetics to identify the molecular pathways that drive cellular behaviour in situ. The authors identify live cell imaging combined with deep molecular profiling of theimaged cells as one possible solution. To this end, the authors establish a novel platform for live cell imaging of tracheal epithelial cells using explants of mouse trachea that allows long-term visualization of cell behaviour, and try to couple live-cell imaging to the transcriptional cell states.

Combining single-cell RNA-seq analyses with live cell imaging offers the unique opportunity to link transcriptional and anatomic, morphological or movement phenotypes of individual cells. To be able to do this in intact tissues at baseline and in response to injury would allow a far more detailed and integral analysis of cellular behaviour in their physiological context. As such, the approach of the authors is interesting and clearly focused on achieving this goal. The only data that can support a claim of successfully achieving this ambitious goal are presented in figure 3, where an advanced mouse model(the Kaede-Green mouse) is used that allows labelling individual cells by photo-conversion, followed by isolation of individual cells by flow cytometry and plate-basedsc RNA-seq analysis of sorted cells. By taking this approach, the authors are able to identify transcriptional differences at the group level between tracheal epithelial cell subsets that differ in their movement after injury.

While this in itself is a remarkable accomplishment, and an interesting observation, the relationship between the 'behaviour' of the cells observed with live cell imaging (the movement after injury) versus the transcriptional phenotype remains rather elusive. One explanation could be that active movement of cells depends on a specific transcriptional program, that is lacking from the non-moving cells. Another explanation could be that the tracheal epithelial cells are inherently heterogeneous, and one subset has the capacity to move whereas others do not, and the transcriptional profile merely identifies these heterogeneous populations. The observation that non-mover cell populations contain both basal and club cells, whereas mover regions only have basal cells seems to support this notion to some extent. However, the authors then claim to use basal-cell derived signatures (excluding the club cells) from mover and non-mover regions and compare this to literature data from another injury model to show that these signatures also identify distinct subsets in a mouse model of polidocanol-induced injury. How the distinction basal vs club cells in the non-mover regions is made remains unclear, and would seem challenging from the number of cells analyzed (as presented in figure 3).

The identification of two behavioural phenotypes of basal cells (mover vs non-mover) in this manuscript is based on group-level phenotypes: the cells belong to a region of moversor a region of non-movers. This is relevant for figures 2 (including supplemental) and 3. In figure 2 supplemental 2C, it seems evident that within one region (or focussing only on all moving regions?), the behaviour of all cells within that region/selection is quite uniform:the variation is really very limited, and all cells seem to speed up and slow down in a highly coordinated fashion within the selected regions shown. At the same time, in figure2D, the distribution of regions across speed categories at 26-36 hours pi (the peak of the movement in suppl 2C) seems almost bimodal, with regions belonging either to non-mover(range 0.5 - 2.5 uM/hr) or mover (range 3.0-7.0 uM/hr) phenotypes. However, all regions display an increased movement at 16h pi compared to the pre-injury movements (Figure2C), indicating that all cells will be induced to induce movement to some extent.

My main concern with this analysis is that the behavioural phenotype of the epithelial cells is assumed to be homogeneous within each region, allowing a contrast to be made in figure3 for the transcriptional phenotypes on the basis of moving phenotypes rather than on the basis of the main variation within the dataset.

For instance, from the t-SNE plot (3B) - for what it's worth of course - and the heatmap (3C) there seems to be at least one non-mover cell that transcriptionally has a higher resemblance to the mover cells than to the other non-mover cells. Of course that can just be the variability present in the dataset, but it could also indicate that non-mover regions are not completely homogeneous, and even more so, that the moving vs non-moving associated transcriptional phenotype is a gradual transition rather than 2 clearly separate sub-phenotypes.

All-in-all, this manuscript describes an interesting technical advance and shows some of the applications thereof. However, the approach also has its limitations: The requirement to mark cells with specific behavioural features for follow-up transcriptomic analysis (such as by photoconversion) necessitates the division of the epithelial cells into major categories on the basis of certain cellular phenotypes (such as movement) that can be visualized by live cell imaging. This limits the analysis opportunities to group-based contrasts in cellular behaviour as also used here by the authors.

Also, the use of explanted tissue is of course less ideal than in vivo imaging, but most likely the only technically feasible approach at this moment. At the same time, the capacity to combine image-based features with single-cell transcriptomic data is an important advance, even when initially only possible in explanted tissue from mouse models carrying all kinds of fluorescent reporters. To strengthen the manuscript, it would therefore be important to discuss the limitations of the approach, as well as to provide a more comprehensive overview of the possible applications that the authors foresee.

We thank the reviewer for the feedback. Our data demonstrates that the movement behavior is an injury-induced phenotype. 24 hours after injury (hpi), the “mover” transcriptional program is transiently enriched, while the “non-mover” transcriptional program is also transiently decreased, consistent with a cell state that is induced by injury (see Figure 4A, 24-hpi).

SO2 removes nearly all the luminal cells (Rock et al., 2009) so we removed the club cells to compare injury response in basal cells. Distinguishing basal vs club cells is done by hierarchical clustering and comparison to established cell type signatures (Montoro et al., 2018). We apologize that the initial presentation did not make this clear. In the revised manuscript, we have provided an additional figure supplement demonstrating the hierarchical clustering (Figure 3 - figure supplement 1A), and the disjoint expression of canonical markers Krt5 (basal) and Scgb1a1 (club), which enabled us to assign unambiguous cell-type identities to discovered clusters (Figure 3 - figure supplement 1B).

We agree with the reviewer that all cells, including cells that we classified as “mover” and “nonmover” are induced to move compared to pre-injury as suggested by Figure 2c. However, “mover” and “non-mover” cells differ dramatically in the amplitude and collective directionality of movement. We investigated the movement phenotypes in detail, including high-resolution imaging at shorter time intervals (10 min). We found that the slow “non-movers” had a large circular directionality variance (akin to oscillations), whereas the rapid “movers” moved directionally across the field of view. We quantified this with particle image velocimetry in Figure 2 – figure supplement 3C-D, and we revised the text to provide additional details about this result.

The reviewer also raises concern about whether the movement is homogeneous enough to account for the variation in the datasets. We used our imaging data to determine the time points in which the mover and non-mover phenotypes varied the most (around 40 hrs post injury) between different regions (Figure 2 - figure supplement 2A, C) but we have also demonstrated that the movement within each region is indeed relatively homogeneous (~200 μm diameter, Movie 1 and Movie 2).

We acknowledge that the presented data did not eliminate the possibility of another main variation within the dataset. We now perform PCA on the dataset, which confirmed that while the first principal component (PC) is associated with a solitary pulmonary neuroendocrine cell, the second PC is strongly associated with the difference between moving and non-moving cells (p=0.003, Wald test). When analyzing only the basal cells, we find that PC-1 provides a very clean separation and overlaps perfectly with the moving vs non-moving distinction (p<2 x 10-16, Wald test, Figure 3 - figure supplemental 2a). Taken together, with this additional analysis we can confirm that our focus on this behavioral phenotype reflects the main variation within the dataset.

We appreciate the reviewer’s nuanced question about the single outlier cell. While we do observe a transcriptional phenotype that is clearly distinct, as the reviewer points out, there is a very small degree of overlap between the two cell type clusters visible on the t-SNE plot in Figure 3B. Given that the physical process of movement is a matter of degree, it is possible that this particular cell is simply not moving as much, and thus activating movement-related transcriptional programs to a lower degree. To analyze this question further in response to this question, we analyzed the separability of these groups by training a machine learning (k-nearest neighbor) classifier to distinguish these clusters (new Figure 3 - figure supplement 2b). We found that the groups could be distinguished with a high accuracy of 98.7% (95% CI: 92.7-99.9) using 5 or more of the signature genes that we defined in Figure 3C. This additional analysis we continue to conclude that while the groups have a very small degree of overlap, the moving and non-moving phenotypes are strongly separable.

We acknowledge the limitations of this approach to groups of cells (see response to Reviewer 1) and both the limitations and advantages of using a tissue rather than cells, and we added these points to the discussion section.

Author Response

Reviewer 1 (Public Review):

1) The finding that thalamic activity exhibits a low dimension structure is in my opinion less of a finding, but rather an assumption that motivates the use of dimensionality reduction techniques. When the authors ask (line 101) "whether thalamic task activity exhibits similar low dimensional structure", what is the alternative hypothesis? I think it is a foregone conclusion that with a restricted number of tasks, and the intrinsic smoothness of fMRI activity data, there are always K<<N components that capture 50,75, 90% of the variance. If you had measured the spiking of the entire population of thalamic neurons or increased the threshold to 99%, the structure of activity would be more high dimensional. So I believe you can either frame this as an assumption going in, or you build carefully an alternative hypothesis of what a "high-dimensional" structure would look like. Generating activity data i.i.d would be the simplest case, but given that both signal and measurement noise in fMRI are reasonably smooth, this would be a VERY trivial null hypothesis.

We thank the reviewer for pointing out this inherent assumption in our analysis. We agree that given the smoothed nature of BOLD signal and the restricted task design we likely cannot effectively test an alternative high dimensional organization hypothesis. We have revised our introduction accordingly and clarify that we use a dimensionality reduction technique with the assumption that we will observe a low dimension structure of thalamic task fMRI data, similar to past fMRI studies that focused on cortical ROIs (line 102). Furthermore, we have revised the discussion section to remove discussion highlighting the low-dimension organization as a novel finding (line 404).

2) The measure of "task hub" properties that is central to the paper would need to be much better explained and justified. You motivate the measure to be designed to find voxels that are "more flexibly recruited by multiple thalamic activity components", but it is not clear to me at this point that the measure defined on line 634 does this. First, sum_n w_i^2 is constrained to be the variance of the voxel across tasks, correct? Would sum_n abs(w) be higher when the weights are distributed across components? Given that each w is weighted by the variance (eigenvalue) of the component across the thalamus, would the score not be maximal if the voxel only loaded on the most important eigenvector, rather than being involved in a number of components? Also, the measure is clearly not rotational invariant - so would this result change after some rotation PCA solution? Some toy examples and further demonstrations that show why this measure makes sense (and what it really captures) would be essential. The same holds for the participation index for the resting state analysis.

Please see our response to essential revision point #1.

3) For the activity flow analysis, the null models (which need to be explained better) appear weak (i.e. no differences across tasks?), and it is no small wonder that the thalamus does significantly better. The Pearson correlations are not overwhelmingly impressive either. To give the reader a feel for how good/bad the prediction actually is, it would be essential that the authors would report noise ceilings - i.e. based on the reliability of the cortical activity patterns and thalamic activity patterns, what correlation would the best model achieve (see King et al., 2022, BioRxiv, as an example).

Please see our response to essential revision point #4.

4) Overall it has not been made clear what the RDM analysis adds to the prediction of the actual activity patterns. If you predicted the activity patterns themselves up to the noise ceiling, you would also hit the RDM correctly. The opposite is not the case, you could predict the correct RDM, but not the spatial location of the activity. However, the two prediction performances are never related to each other and it remains unclear what is learned from the latter (less specific) analysis.

We agree that the utility of the RDM analysis is not clear, and we have removed it from the manuscript.

Author Response

Reviewer #1 (Public Review):

This paper details the creation and data behind the website http://pandemics.okstate.edu/covid19/. The authors attempt to explore if there is a cause and effect between the detection of unusually increased mutation activity in the genomic surveillance databases and subsequent near-term surges in SARS-CoV-2 case numbers.

Overall the premise is interesting as other than following case numbers reported to health authorities and observing what is happening in another country, there is no reliable way to predict when a surge is going to occur. Unfortunately, the data demonstrate that there was no reliable metric that could be used to predict surge events. Interestingly, the website has issued a "surge alert" currently for the month of September. It will be interesting to observe whether their model indeed has predictive power or whether the current analysis is merely coincidental with the surges but not necessarily predictive of them.

In this work, we investigated a number of metrics for finding a reliable signal of surge prediction. The commonly used ratio ka/ks or the derivative of ka/ks with respect to time did not provide a reliable metric. However for the same data, ka has provided a fairly robust surveillance signal so far. We believe ka/ks studies provide insights into genome changes, but not as a function of short time periods such as days (at least not in the case of SARS-CoV-2). As the motivation of our work is to provide the community with a genomic surveillance approach in real time, we believe that the current data shows that ka is, at present, a useful and fairly reliable metric.

As the reviewer mentioned, while this manuscript was being reviewed, we issued a warning on September 7th 2022. Several different types of data (including number of new infections, number of hospitalizations, and COVID19 related deaths) has indicated that our warning was accurate since there was a surge in reported number of cases in September and reached a peak in October. For instance, plots shown in Figure S6 indicate that there was a surge in number of cases around Europe at large, and several individual countries including France, United Kingdom, Germany and Italy. Similarly our earlier warning in June also was followed by surges being reported across many countries and collectively across the world (Figure S5). Therefore, we believe the presented methodology has been validated.

Reviewer #2 (Public Review):

In this manuscript, Najer et al., perform a comprehensive bioinformatic analysis of SARS-CoV-2 sequences available from public repositories. Through a comparison with the genome sequence of the original Wuhan 2020 strain, they identify the total accumulation of non-synonymous mutations as a predictor of the evolution of new strains. The manuscript provides data for three structural proteins - spike (S), membrane (M), and envelope (E) proteins, as well as data for the non-structural RNA-dependent RNA polymerase (RDRp) protein that serves as a negative control. However, the predictivity of this approach is most marked only for the Omicron variant, with considerable variation in the predictive power of SARS-CoV-2 proteins for other variants. Focusing on a spike, the method does not detect the alpha variant or delta variant surges, which were mostly driven by changes in spike protein, although the level of sequencing data available for the delta variant might have been less. Notably, although the authors conclude that other parameters such as the ratio of non-synonymous to synonymous mutations or the rate of accumulation of non-synonymous mutations are not predictive, they appear to have similar success in predicting the omicron surge.

We agree with the reviewer, the case of spike protein during the Alpha surge could have been affected by insufficient number of sequences. In case of Gamma/Delta variants, we did notice changes in the spike and the membrane protein. For the case of Omicron and its various sub-variants, the use of ka provides a reliable signal due to changes in the spike, membrane and envelope proteins.

**Author Response""

Reviewer #2 (Public Review):

The work systematically reassesses fungal mi/miRNA-like characteristics and annotation confidence and identifies that many of the loci fail to meet the key points of the methods developed for animal or plant miRNAs. Therefore, the authors establish a set of criteria suitable for the annotation of fungal miRNAs and provide a centralized annotation of identified mi/milRNA hairpin RNAs in fungi based on their established rules.

Here are some comments and suggestions for the manuscript to be improved:

1) The title mentions "ancestral links", however, the main context of this paper does not include the evolution of fungal mi/milRNAs or show the origins of conserved mi/milRNAs in fungi. The authors are suggested to consider a more appropriate title for this work.

Agreed, we have modified our title to include a more fitting description of the outcome of the study:

“Comprehensive re-analysis of hairpin small RNAs in fungi reveals loci with conserved links”

2) The work proposes a fungal mi/milRNAs hairpin precursor recovery pipeline with three minimal criteria to annotate fungal mi/milRNA loci, which allows nearly half of the loci to pass these rules. To highlight the innovation of this annotation, it is strongly suggested that the authors compare their established pipeline and criteria for fungi with those used in animal or plant miRNAs in detail, and emphasize the advantages of the established pipeline. A figure showing the established pipeline and detailed parameters is needed.

We have now included a clear workflow diagram for establishing miRNA annotation records and confidence tiers (Figure 1-supplemental 3). As for the comparison with rules in plants and animals, this is stated in Table S6, where it shows some rules employed by other tools/papers/species. We believe these combined supplementals give a strong overview of our approach and how it differs from rules in other approaches.

3) The established "standard rules" for fungal mi/milRNA annotation still require more evaluation. It would be better if there is experimental validation to improve confidence.

Sequencing evidence is generally regarded as the gold-standard of experimental support for identifying and annotating miRNAs (Axtell and Meyers, 2018) though the rules are not clear yet in fungi. We agree that developing a standard-rule-set is a high-priority for identifying complete annotation standards. We had a statement (~ line 290) affirming this need, and have now modified this sentence to highlight the need for a sufficient standard.

“While this minimal rule-set is useful for filtering the lowest-confidence loci, it is likely not sufficient to form the basis of an annotation and this analysis further confirms the need for a standardized pipeline and set of criteria for miRNA annotation in fungi.”

To address the question of experimental validation, we have included descriptions of loci with strong-functional support in Table S5, including a section discussing top-tier loci in the discussion, described in the response to reviewer 3.

Author Response

Reviewer #1 (Public Review):

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public Review):

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

Strength and Limitation

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Author Response

Reviewer #1 (Public Review):

The authors are trying to determine how time is valued by humans relative to energy expenditure during non-steady-state walking - this paper proposes a new cost function in an optimal control framework to predict features of walking bouts that start and stop at rest. This paper's innovation is the addition of a term proportional to the duration of the walking bout in addition to the conventional energetic term. Simulations are used to predict how this additional term affects optimal trajectories, and human subjects experiments are conducted to compare with simulation predictions.

I think the paper's key strengths are its simulation and experimental studies, which I regard as cleverly-conceived and well-executed. I think the paper's key weakness is the connection between these two studies, which I regard as tenuous for reasons I will now discuss in detail.

The Title asserts that "humans dynamically optimize walking speed to save energy and time". Directly substantiating this claim would require independently manipulating the (purported) energy and time cost of walking for human subjects, but these manipulations are not undertaken in the present study. What the Results actually report are two findings:

1. (simulation) minimizing a linear combination of energy and time in an optimal control problem involving an inverted-pendulum model of walking bouts that (i) start and stop at rest and (ii) walk at constant speed yields a gently-rounded speed-vs-time profile (Fig 2A);

2. (experiment) human subject walking bouts that started and stopped at rest had self-similar speed-vs-time profiles at several bout lengths after normalizing by the average duration and peak speed of each subject's bouts (Fig 4B).

If the paper established a strong connection between (1.) and (2.), e.g. if speed-vs-time trajectories from the simulation predicted experimental results significantly better than other plausible models (such as the 'steady min-COT' and 'steady accel' models whose trajectories are shown in Fig 2A), this finding could be regarded as providing indirect evidence in support of the claim in the paper's Title. Personally, I would regard this reasoning as rather weak evidence - it would be more accurate to assert 'brief human walking bouts look like trajectories of an inverted-pendulum model that minimize a linear combination of energy and time' (of course this phrasing is too wordy to serve as a replacement Title -- I am just trying to convey what assertion I think can be directly substantiated by the evidence in the paper). But unfortunately, the connection between (1.) and (2.) is only discussed qualitatively, and the other plausible models introduced in the Results are not revisited in the Discussion. To my naive eye, the representative 'steady min-COT' trace in Fig 2A seems like a real contender with the 'Energy-Time' trace for explaining the experimental results in Fig 4, but this candidate is rejected at the end of the third-to-last paragraph in the 'Model Predictions' subsection of Results based on the vague rationale that is never revisited.

We have addressed most of this comment above, but respond here regarding Fig. 4. The argument against steady min-COT should also point out the peak speed. The Results have been revised thus: “In contrast to the min-COT hypothesis, the human peak speeds increased with distance, many well below the min-COT speed of about 1.25 m/s. The human speed trajectories did not resemble the trapezoidal profiles of the steady min-COT hypothesis for all distances, nor the triangular profiles of steady acceleration.”

An additional limitation of the approach not discussed in the manuscript is that a fixed step length was prescribed in the simulations. The 'Optimal control formulation' subsection in the Methods summarizes the results of a sensitivity analysis conducted by varying the fixed step length, but all results reported here impose a constant-step-length constraint on the optimal control problem. Although this is a reasonable modeling simplification for steady-state walking, it is less well-motivated for the walking bouts considered here that start and stop at rest. For instance, the representative trial from a human subject in Figure 8 clearly shows initiation and termination steps that differ in length from the intermediate steps (visually discernable via the slope of the dashed line interpolating the black dots). Presumably different trajectories would be produced by the model if the constant-step-length constraint were removed. It is unclear whether this change would significantly alter predictions from either the 'Energy-Time' or 'steady min-COT' model candidates, and I imagine that this change would entail substantial work that may be out of scope for the present paper, but I think it is important to discuss this limitation.

This is addressed elsewhere (Essential Revisions 2), but we explain more here. One of the parameter studies included step length increasing with speed according to the human preferred relationship. This is included in Fig. 3, and so we concluded that variable step lengths are not critical to the speed trajectories. A related assumption is that the energetic cost of modulating step length/frequency is small compared to the step-to-step transition cost. We believe that humans expend substantial energy for both costs, but that the overall cost of walking is still dominated by step-to-step transitions.

With my concerns about the paper's framing and through-line noted as above, I want to emphasize that I regard the computational and empirical work reported here to be top-notch and potentially influential. In particular, the experimental study's use of inexpensive wearable sensors (as opposed to more conventional camera-based motion capture) is an excellent demonstration of efficient study design that other researchers may find instructive. To maximize potential impact, I encourage the authors to release their data, simulations, and details about their experimental apparatus (the first two I regard as essential for reproducibility - the third a selfless act of service to the scientific community).

I think the most important point to emphasize is that the bulk of prior work on human walking has focused on steady-state movement - not because of the real-world relevance (since one study reports 50% of walking bouts in daily life are < 16 steps as summarized in Fig 1B), but rather because steady walking is a convenient behavior to study in the laboratory. Significantly, this paper advances both our theoretical and empirical understanding of the characteristics of non-steady-state walking.

It is also significant to note the relationship between this study, where time was incorporated as an additive term in the cost of walking, with previous studies that incorporated time in a multiplicative discount in the cost of eye and arm movements. There is an emerging consensus that time plays a key role in the generation of movement across the body - future studies will discern whether and when additive or multiplicative effects dominate.

We have acknowledged this in a brief sentence: “Indeed, we have found a similar valuation of time to explain how reaching durations and speed trajectories vary with reaching distance (Wong et al., 2021).” As an aside, in that reference we measured metabolic cost of cyclic arm reaching, combined it with a linear time cost, and predicted reaching durations vs. distance and bell-shaped hand speed trajectories. Others (Shadmehr et al. Curr Biol. 2016) have proposed multiplicative (hyperbolic) temporal discounting to explain durations, but the cost formulas are not dynamical, and cannot produce trajectories. We agree with reviewer’s point, but we think the evidence for hyperbolic discounting is not strong. Linear time costs are simpler and work at least as well. This is of great interest to us, but we didn’t discuss beyond the brief mention above, because we fear it is too far afield.

Reviewer #2 (Public Review):

This paper provides a novel approach to quantifying the tradeoff between energetic optimality during walking and the valuation of time to travel a given distance. Specifically, the authors investigated the relationships between walking speed trajectories, distance traveled, and the valuation of (completion) time. Time has been proposed as a potential factor influencing movement speed, but less is understood about how individuals balance energetic optimality and time constraints during walking. The authors used a simple, sagittal-plane walking model to test competing hypotheses about how individuals optimize gait speed from gait initiation to gait termination. Their approach extends literature in the space by identifying optimal gaits for shorter, partially non-steady speed walking bouts.

The authors successfully evaluated three competing walking objectives (constant acceleration, minimum cost of transport at steady speed, and the energy-time objective), showing that the energy-time objective best matched experimental data in able-bodied adults. Although other candidate objectives may exist, the paper's findings provide a likely-generalizable explanation of how able-bodied humans select movement strategies that encompass studies of steady-speed walking.

Overall, this paper provides a foundation for future studies testing the validity of the energy-time hypothesis for human gait speed selection in able-bodied and patient populations. Extensions of this work to patient populations may explain differences in walking speed during clinical assessments and provide insight into how individual differences in time valuation impact performance on assessments. For example, understanding whether physical capacity or time valuation (or something comparable) better explains individual differences in walking speed may suggest distinct approaches for improving walking speed.

Strengths:

The authors presented a compelling rationale for the tradeoffs between energetic optimality and time and their results provide strong support for a majority of their conclusions. In particular, significant reductions in the variance of experimental speed trajectories provides good support for the scaling of speeds across individuals and the plausibility of the energy-time hypothesis. Comparison to theoretical (model-based) reductions across difference time valuation (cT) parameters would further enhance confidence in the practical significance of the variance reductions. Further, while additional work is needed to determine the range of "normal" valuations of time, the authors present experimental ranges that appear reasonable and are well explained. The computational and analytical methods are rigorous and are supported by the literature. Overall, the paper's conclusions are consistent with experimental and computational results.

The introduction of a model-based analytical approach to quantify the effects of time valuation of walking could generalize to test other cost functions, populations, or locomotion modes. Further, models of varying complexity could be implemented to test more individualized estimates of metabolic cost, ranging from 3D dynamic walking models (Faraji et al., Scientific Reports, 2018) or physiologically-detailed models (Falisse et al., Journal of The Royal Society Interface. 2019). The relatively simple set of analyses used in this paper is consistent with prior literature and should generalize across applications and populations.

The authors justified simplifications in the analysis and addressed major limitations of the paper, such as using a fixed step length in model predictions, using a 2D model, and basing energy estimates on the mechanical work of a simple model. It is unlikely that the paper's conclusions would change given additional model complexity. For example, a 3D walking model would need to control frontal plane stability. However, in able-bodied adults, valuation of frontal-plane stability during normal walking would not likely alter the overall shape of the predicted speed profiles.

Weaknesses:

The primary weakness of this work is that alternative objectives may provide similar speed profiles and thus be plausible objectives for human movement. For example, the authors tested an objective minimizing the steady-speed cost of transport. This cost function is consistent with the literature, but (as predicted) unlikely to explain acceleration and deceleration during gait. An objective more comparable to the energy-time hypothesis would be to minimize the net energy cost over the entire bout, including accelerations and decelerations. This may produce results similar to the energy-time hypothesis. However, a more complex model that incorporates non-mechanical costs (e.g., cost of body weight support) may be needed to test such objectives. Therefore, the energy-time hypothesis should be considered in the context of a simple model that may be incapable of testing certain alternative hypotheses.

We have addressed some of this comment in Essential Revisions 4.

We are unsure what is meant by “net energy over the entire bout, including accelerations and decelerations.” Our hypothesis uses total (gross) energy over the entire bout, and already includes accelerations and decelerations. If “net” refers to the customary definition of metabolic energy minus resting, then it differs from our gross cost (Fig. 6A) only in the amount of constant offset, namely resting cost. Removing the offset is equivalent to a decrease in C_T. As shown in Fig. 3, this would reduce peak speeds magnitudes but not change the shape of the speed, peak speed, and duration patterns. There is also another interpretation where the cost of walking includes only net energy, and the cost of time includes the resting metabolic rate (Fig. 6C). This interpretation yields the same predictions, the only difference is whether resting rate is treated as an energy or a time cost. We have not made further changes, because we are unsure what the reviewer meant. The difference between net and total is at most one of degree, not of qualitatively different behavior.

We do not address the proposed “cost of body weight support” because we are unsure of the definition. There is a hypothesis by Kram & Taylor (1990) that defines a metabolic cost rate proportional to body weight divided by ground contact time. It is unclear if this is what reviewer is referring to, so we did not include it in the manuscript. However, IF this is what reviewer means, we do not consider the Kram & Taylor (“K&T”) cost to be a viable hypothesis for computational models. It is a correlation observed from data, which is inadequate as a model, for several reasons. First, in a model optimization, it leads to absurd predictions, because metabolic cost could then be reduced simply by increasing stance (contact) time. A model could do so simply by walking with very long double support phases, or running with a very brief aerial phase, both of which people clearly do not do. In walking, extended double support durations result in much higher metabolic cost (Gordon et al., APMR 2009). Models must operate quite literally on whatever objective they are given, and here, a literal interpretation of K&T makes absurd predictions.

Another issue with the K&T cost is that it is not mechanistic. A mechanistic model is concerned with the forces and work performed by an actuator such as muscle. Muscles experience forces far greater than body weight, not captured by the K&T cost. Of course, overall cost for animal locomotion is roughly proportional to body weight, but what a model needs is a cost associated with its control inputs, e.g. actuator forces.

We have also examined the K&T hypothesis in previous publications. In Schroeder & Kuo (Plos Comp Biol 2021), we used a simple model of running that minimizes an energetic cost dominated by mechanical work. Even though the model has no cost similar to K&T, its predicted metabolic cost is correlated with the K&T cost. Correlation does not imply causation, which is known in this model.

We have also examined the K&T hypothesis in experimental data. In Riddick & Kuo (Sci Rep 2022), we examined human data and found that there are many variables that correlate quite well with metabolic cost, including the K&T correlate. We use human data to show how mechanical work could explain metabolic cost, and even if it does, the K&T cost appears as a correlate. In our interpretation, both model and data that experience an energetic cost proportional to mechanical work may have a number of variables correlated to energy cost. Those correlates need not have any causal influence.

There are, of course, many similar correlates that could be or have been proposed to explain the metabolic cost of running. Most such correlates are not operational enough to work in a model, and it is also difficult to predict what a reader might consider plausible, even if we do not.

We agree with this statement: “the energy-time hypothesis should be considered in the context of a simple model that may be incapable of testing certain alternative hypotheses.” In fact, in Discussion of limitations we listed other potential factors (e.g. forced leg motion, stability, 3D motion), and stated “We did not explore more complex models here, but would expect similar predictions to result if similar, pendulum-like principles of work and energetic cost apply.” We had also cited other models that include such factors and are compatible with the step-to-step transition concept. Finally, we already stated, “the Energy-Time hypothesis should be regarded as a subset of the many factors that should govern human actions, rendered here in a simple but quantitative form.” We believe this is already aligned with reviewer’s comment.

An experimental design involving an intervention to perturb the valuation of time would provide stronger support for time being a critical factor influencing gait speed trajectories. The authors noted this limitation as an area of future work.

While the results are compelling, the limited sample size and description of participants limit the obvious generalizability of the results. Older adults tend to have higher metabolic costs of walking than younger adults, which may alter the predicted time-energy relationships (Mian OS, et al., Acta physiologica. 2006). As noted in the introduction, differences in walking speeds have been observed in different living environments. General information on where participants lived (city, small town, etc...) may provide readers with insight into the generalizability of the paper's conclusions. Additionally, the experimental results figures show group-level trends, but individual-specific trends and the existence of exceptional cases are unclear.

We wish to defend the “limited sample size.” The present sample size was (in our opinion) sufficient to test the hypothesis, and we have reported confidence intervals and other statistics where appropriate. (As always, it is up to the individual reader to decide whether they are convinced or not.) It is true that the data may be insufficient for other purposes, but we cannot anticipate or address all other purposes.

We appreciate the relevant connection to aging. We have added to Discussion, “We do not know whether that family [of trajectories] also applies to older adults, who prefer slower steady speeds and expend more energy to walk the same speed (Malatesta, 2003). Perhaps an age-related valuation of time might explain some of the differences in speed.”

We agree about the participants, and have added “Subjects were recruited from the community surrounding the University of Calgary; the city has a moderately affluent population of about 1.4 M, with a developed Western culture.”

No specific reviewer recommendation was made about individual-specific trends, but there are several indicators already included in the manuscript. First, all trials from all subjects are shown in Fig. 4A. Any truly exceptional cases should be visible as substantial deviations from the group. Second, the normalization by peak speed in Fig. 4B shows how individuals tend to be fairly consistent in their preferred speeds, in that shorter and longer bouts of an individual are consistent with each other, even if some walk faster than others. Third, this observation is analyzed more quantitatively by the reduction in standard deviations with normalization (Results). Fourth, we will provide a data repository with all the data, to allow readers to inspect individuals more carefully (Data availability statement).

The authors' interpretation of clinical utility is vague and should be interpreted with caution. A simple pendulum-based walking model is unlikely to generalize to patient populations, whose gait energetics may involve greater positive and negative mechanical work (Farris et al., 2015; Holt et al., 2000). Additionally, the proposed analytical framework based on mechanical work as a proxy for the metabolic cost may not generalize to patient populations who have heterogeneous musculotendon properties and increased co-contraction (e.g., children with cerebral palsy; Ries et al., 2018). Consequently, the valuation of time for an individual could be incorrectly estimated if the estimates of metabolic cost were inaccurate. Therefore, as the authors noted for their able-bodied participants, more precise measures of metabolic rates will be critical for translating this work into clinical settings.

We agree, and did not intend to say that clinical populations must walk the same way, rather that the Normal patterns could be used as a basis of comparison. To make this clearer, we have amended the Discussion of clinical implications (new text emphasized): “it may be possible to predict the duration and steady speed for another distance, referenced from a universal family of walking trajectories. We have identified one such family that applies to healthy individuals with pendulum-like gait. Of course, some clinical conditions might be manifested by a deviance from that family, perhaps in the acceleration or deceleration phases, or in how the trajectories vary with distance. If quantified, such deviance might prove clinically useful… the characterization of distance-dependent speed trajectories can potentially provide more information than available from steady speed alone.”

We agree that the valuation of time can be inaccurate if the metabolic cost is inaccurate. That is why we did not make a precise estimate of the valuation. We have amended the text to help clarify that our rough estimates are based on previous data. In addition, our general scientific intent is to reveal behavioral sensitivities, for example of walking duration to bout distance, as opposed to absolute numerical quantities.

Author Response

Reviewer #2 (Public Review):

One other major concern I have regards the conclusion that the participants in these studies use an additive rather than a multiplicative rule to integrate the risk information. The additive rule is problematic in general because it fails to predict the reversal in the effect of probability on payoffs when the payoffs change sign. More specifically, increasing the probability of winning increases the probability of choosing an option when the payoff is positive, but the effect reverses when the payoff is negative. One needs to impose some pretty ad hoc assumptions to make the additive model account for this fundamental interaction between probability and payoff. Of course, the experiments reported here did not include negative payoffs, and so didn't run into this problem. In fact, when the payoffs are positive, it is possible to transform the multiplicative model to an additive model by a log transform. This transformation is only possible for the simple type of gamble investigated in this manuscript - a single amount to win with some probability of winning, otherwise win or lose nothing. If the gambles involved more than one outcome, then the theorist needs to deal with a sum of products and the log transform is no longer possible. For these reasons I am very skeptical about the general application of a summation rule for probability and value in risk choice. The authors do address this issue to some extent. They point out the abundance of other research supporting a multiplicative rule, and they speculate that the additive rule may have occurred within the restrictions of this special situation. The latter discussion is a good start, but I suggest that the authors discuss this fundamental issue in more depth.

Thank you for this very insightful comment. We have now included more in-depth discussions about the decision rules (multiplicative vs. additive) in our Discussion, in which we have absorbed and reflected many of the insights offered by Reviewer #2.

Author Response

Reviewer #1 (Public Review):

This paper tests the hypothesis that 1/f exponent of LFP power spectrum reflects E-I balance in a rodent model and Parkinson's patients. The authors suggest that their findings fit with this hypothesis, but there are concerns about confirmation bias (elaborated on below) and potential methodological issues, despite the strength of incorporating data from both animal model and neurological patients.

First, the frequency band used to fit the 1/f exponent varies between experiments and analyses, inviting concerns about potentially cherry-picking the data to fit with the prior hypothesis. The frequency band used for fitting the exponent was 30-100 Hz in Experiment 1 (rodent model), 40-90 Hz in Experiment 2 (PD, levodopa), and 10-50 Hz in Experiment 3 (PD, DBS). Ad-hoc reasons were given to justify these choices, such as " to avoid a spectral plateau starting > 50 Hz" in Experiment 3. However, at least in Experiment 3 (Fig. 3), if the frequency range was shifted to 1-10 Hz, the authors would have uncovered the opposite effect, where the exponent is smaller for DBS-on condition.

We agree that parameter choice is crucial, in particular, choice of the fitting range. In addition to the 40-90 Hz range (Figure 2C), we have performed aperiodic fitting for five other frequency ranges to test to what extent the reported results are sensitive to the selected frequency range (Figure S2A). This analysis showed that the results are robust when a broad frequency range from 30 to 95 Hz was chosen, which is consistent with what has been suggested by Gao et al., 2017 to make inferences on the E/I ratio.

Accordingly, we have now repeated the analyses for the animal data with the same fitting range used for the ON-OFF medication comparison in humans. Along with Figure S2A where different frequency ranges were tested for data used in Figure 2, this shows that the results in Figure 1 and 2 hold up with higher aperiodic exponents when STN spiking is low and vice versa. Therefore, a broad fitting range from 30 to 90 Hz (excluding harmonics of mains interference) generates consistent results for both human and animal data.

We opted against a fitting range from 1-10 Hz because of two restraints highlighted in Gerster et al., 2022. First, a fitting range starting at 1 Hz could have a larger y-intercept due to the presence of low-frequency oscillations. This could lead to a larger aperiodic exponent and could be misinterpreted as stronger neural inhibition. Therefore, the lower fitting bound should be chosen to best avoid known oscillations in the delta/theta range (Gerster et al., 2022). Second, frequencies should be chosen to avoid oscillations crossing fitting range limits. In Figure 3A, oscillations in the theta/alpha band both ON and OFF stimulation would complicate parameterisation and would likely result in spurious fits.

We also tested the effect of changing the peak threshold, peak width limits and the aperiodic fitting mode on FOOOF parameterisation. Increasing and decreasing the peak threshold from its default value (at 2 standard deviations) did not change results (Figure S2B). Similarly, adapting the peak width limits did not affect the exponent difference between medication states (Figure S2C). Finally, choosing the ‘knee’ mode instead of ‘fixed’ resulted in fundamentally different aperiodic fits that did not differ anymore with medication (Figure S2D). This is most likely a consequence of the near linear PSD in log-log space from 40 to 90 Hz (Figure 2B). If there is no bend in the PSD, the FOOOF algorithm will be forced to assign a ‘random’ knee and the aperiodic fit will then mostly reflect the slope of the spectrum above the knee point.

Second, there are important, fine-grained features in the spectra that are ignored in the analyses, which confounds the interpretation.

One salient example of this is Fig. 2, where based on the plots in B, one would expect that the power of beta-band oscillations to be higher in the Med-On condition, as the oscillatory peaks rise higher above the 1/f floor and reach the same amplitude level as the Med-OFF condition (in other words, similar total power is subtracted by a smaller 1/f power in the Med-ON condition). But this impression is opposite to the model-fitting results in C, where beta power is lower in the Med-ON condition.

We agree that PSDs over a broad frequency range (e.g. 5-90 Hz) typically do not have a single 1/f property. Instead, there can be multiple oscillatory peaks and ‘knees/bends’ in the aperiodic component. For these cases, fitting should be performed using the knee mode. To extract periodic beta power, we parameterise the PSD between 5 and 90 Hz and select the largest oscillatory component between 8 and 35 Hz (this range was extended to include the large oscillatory peaks in hemispheres 27 and 28 at ~ 10 Hz, see Figure R1). We now use the knee mode, to model the aperiodic component between 5 and 90 Hz when periodic beta power is calculated (see our previous comments). Figure R1 provides an overview of all PSDs ON and OFF medication, the aperiodic fits (5-90 Hz (knee) and 40-90 Hz (fixed)) and the detected beta peaks. In spite of this modification in our pipeline, periodic beta power is still larger OFF medication (Figure 2C), in keeping with previous studies (Kim et al., 2022; Kühn et al., 2006; Neumann et al., 2017; Ray et al., 2008). We acknowledge the reviewer’s point that the average spectra in Figure 2B are misleading in that respect and for clarity provide here all 30 spectra in both conditions. Note that the calculation of aperiodic exponents between 40 and 90 Hz is not affected by this change in our pipeline. Figures 2B, D+E were revised accordingly.

We have repeated the analysis of our animal data using the ‘knee mode’ with a fitting range from 30 to 100 Hz. However, using the knee mode did not improve the goodness of fit or fitting error and, in fact, made them slightly worse (Figure S5). Based on this, we think the fixed mode would provide a more holistic model for the PSDs used in this analysis. We have now added this comparison in Figure S5 to justify the choice of the fixed mode.

Figure R1. PSDs from all 30 hemispheres ON and OFF medication. Aperiodic fits are shown between 5-90 Hz (knee mode), which was used to calculate the power of beta peaks, and between 40-90 Hz (fixed mode), which was used to estimate the aperiodic exponent of the spectrum.

Another example is Fig. 1C, where the spectra for high and low STN spiking epochs are identical between 10 and 20 Hz, and the difference in higher frequency range could be well-explained by an overall increase of broadband gamma power (e.g. as observed in Manning et al., J Neurosci 2012, Ray & Maunsell PLoS Biol 2011). This increase of broadband gamma power is trivially expected, as broadband gamma power is tightly coupled with population spiking rate, which was used to define the two conditions.

We agree with the reviewer that in Figure 1C, high and low STN spiking states could well be separated by average gamma power (Figure 1E), too. However, the difference of aperiodic exponents is more prominent between both conditions (Figure 1D+E, based on p-values). What is more, in human LFP data recorded from clinical macroelectrodes, medication states can be reasonably well distinguished using the aperiodic exponent between 40-90 Hz (Figure 2C), but average gamma power does not separate both states (Figure S3A). This suggests that the aperiodic exponent reflects more than just power differences in the high gamma regions. In addition, power changes do not inevitably change the aperiodic exponent and vice versa as elaborated in (Donoghue et al., 2020).

Manning et al., 2009 show that the power spectrum is shifted to higher power values at all observed frequencies (2-150 Hz) as firing rates increase. As the reviewer points out, power spectra of our data are almost identical between 10-20 Hz (despite the marked spiking differences) and only drift apart from > 20 Hz (Figure 1C). This is a relevant difference between our study and Manning et al., 2009 and suggests that power differences in the gamma range are not solely explained by differences in spiking. This is confirmed when cortical activity at different spikes/sec is modelled (Miller et al., 2009). The entire spectrum is shifted to higher power values if spiking rates increase.

Ray & Maunsell, 2011 reported low (30-80 Hz) and high (> 80 Hz) gamma activity in the macaque visual cortex, with a positive correlation between spiking activity and high gamma activity. However, activities in the low gamma range (30-80 Hz), which largely overlaps with the frequency range in our study, does not necessarily correlate with firing rates.

In conclusion, the link between gamma power and spiking activity is not as strong as alluded. Even if the change in spiking activities can lead to changes of both gamma power and the aperiodic exponent, the aperiodic exponent would still constitute a measure to separate E/I levels and medication states.

The above consideration also speaks to a major weakness of the general approach of considering the 1/f spectrum a monolithic spectrum that can be captured by a single exponent. As the authors' Fig. 1C shows, there are distinct frequency regions within the 1/f spectrum that have different slopes. Indeed, this tripartite shape of the 1/f spectrum, including a "knee" feature around 40-70 Hz which is well visible here, was described in multiple previous papers (Miller et al., PLoS Comput Biol 2009; He et al., Neuron 2010), and have been successfully modeled with a neural network model using biologically plausible mechanisms (Chaudhuri et al., Cereb Cortex, 2017). The neglect of these fine-grained features confounds the authors' model fitting, because an overall increase in the broadband gamma power - which can be explained straightforwardly by the change in population firing rates - can result in the exponent, fit over a larger spectral frequency region, to decrease. However, this is not due to the exponent actually changing, but the overall increase of power in a specific sub-frequency-region of the broadband 1/f activity.

We have now used the knee mode for aperiodic fits between 5 and 90 Hz when periodic beta power is calculated. We agree that this broad frequency range is unlikely to have a single 1/f component.

We have also repeated the analysis of our animal data using the knee mode for aperiodic fits between 30 and 100 Hz (Figure S5). However, the goodness of fits had barely changed. In fact, the R2 and error become slightly worse. In addition, the knee parameter complicates interpretation of the aperiodic exponent and has to be considered along with the knee frequency. What is more, we do not see this bend around 40-70 Hz in all subjects. We show PSDs of representative LFP channels in Figure R2 and need to assert that the knee around 40-70 Hz is not a robust finding in our data set. Therefore, we chose the fixed mode for parameterisation within this frequency band.

Please see our answer to the previous comment regarding the link between broad gamma power and changes in population firing rates.

Figure R2. PSDs of representative PSD channels for each animal (data used in Figure 1C). The knee around 40-70 Hz is not a robust finding in all PSDs.

Author Response

Reviewer #3 (Public Review):

Argenty et al. investigated the role of Lissencephaly gene 1 (LIS1), a dynein-binding protein, in thymic development and T cell proliferation. They find that LIS1 is essential for the early stages of T and B cell development, and demonstrate that loss of LIS1 has a negative impact on the transition from DN3 to DN4 thymocytes and on the maturation of pre-pro-B cells into pro-B cells in the bone marrow. Using a CD2Cre Lis1fl/fl murine model, they observe that in thymocytes LIS1 is critical for DN3 proliferation and completion of cell division. Then, using a CD4Cre Lisfl/fl model (Cd4 promoter is up-regulated just in later stages of thymic development and, thus, does not impact DN3 thymocytes) they show that LIS1-deficient CD4 T cells have proliferation defects following both TCR-dependent or -independent stimulation, which results in apoptosis. They also confirm previous reports that show that LIS1-deficient CD8 T cells do not have their proliferation impaired upon TCR stimulation, which suggests that these two cell types rely on different mechanisms to regulate the cell cycle. Finally, the authors make efforts to determine how LIS1 regulates proliferation in thymocytes and CD4 T cells. Interestingly, they show that LIS1 is important for chromosome alignment and centrosome integrity and provide data that support a model where LIS1 would facilitate the assembly of active dyneindynactin complexes. These data provide interesting insights into how different cell types use distinct strategies to undergo mitosis and how this can impact on their proliferation and fate decisions. The conclusions of the manuscript are mostly supported by the provided data, although certain aspects can be further investigated and clarified.

Strengths of the paper:

By combining a re-assessment of previous reports with new findings, the data from this manuscript convincingly demonstrates that LIS1 is crucial for cell proliferation in certain development steps/cell types. Furthermore, the manuscript provides clear evidence of how LIS1 loss causes proliferation defects by disrupting centrosome integrity and chromosome alignment both in CD4+ T cells and thymocytes.

Weakness of the paper:

Although authors successfully address the mechanistic role of LIS in thymocyte and CD4+ T cell division, the manuscript would be strengthened by both providing further evidence to support some of their conclusions and a review of some speculations raised in the discussion.

In Figure 1, the authors claim that LIS1 is not required for pre-TCR assembly, but for expansion/proliferation of DN3 thymocytes as a step prior to reaching the DN4 stage. However, authors indeed observe increased expression of CD5 (which is a downstream event of Notch and IL-7R signalling). Thus, from the data provided it is not clear whether signalling through Notch or IL-7R is definitely not affected, which could be clarified by assessing the expression of other downstream targets of these molecules.

CD5 is a downstream target of the pre-TCR signaling but to our knowledge, it is not a downstream target of Notch or IL-7R signaling. The sentence p7 of the initial manuscript was re-formulated since we understand that it could be misleading. However, we fully agree with the reviewer’s comment on Notch and IL-7R signaling and included new data in the revised version of the manuscript to address this point. Notch signaling stimulates metabolic changes which lead to the increase of thymocyte cell-size following the b-selection checkpoint (Ciofani M. et al., Nature Immunology, 2005; Maillard I. et al., The Journal of Experimental Medicine, 2006) and to the up-regulation of the transferrin receptor CD71 (Kelly, A.P. et al., The EMBO journal, 2007). We now show in Figure 1E of the revised manuscript that the loss of LIS1 does not affect the average cell-size of post-b-selection thymocytes and the expression level of CD71 in these cells, suggesting that Notch signaling is preserved in the absence of LIS1. This was confirmed in vitro following stimulation of DN3a thymocytes with OP9-dl1 cells (Figure 2D of the revised manuscript). In this Figure, we also analyzed the expression level of Bcl-2, which is regulated by IL-7R signaling (von Freeden-Jeffry, U. et al., Immunity, 1997). We show that Bcl-2 is comparable in abundance in LIS1 wild-type and LIS1-deficient thymocytes following stimulation with OP-9dl1, suggesting that Il-7R signaling is not affected by the absence of LIS1.

In Figure 3, the authors mostly confirm previous data from Ngoi, Lopez, Chang, Journal of Immunology, 2016 (reference 34), but also provide evidence of a role of LIS1 in CD4+ T cell proliferation in more physiological setups, using OT2-CD4-Cre Lis1flox/flox (or OT2 Lisflox/flox as controls) in adoptive transfer experiments followed by antigen-specific immunization. However, the evidence provided by the authors about proliferation defects in LIS1-deficient cells in this context is limited by the early timepoint chosen: day 3 post-immunization.

We choose to analyze CD4+ T cells at day 2 and 3 after immunization because we sought to catch early cell-division waves through CTV dilution. We also wanted to show that LIS1 deficient CD4+ T cells could normally survive and migrate to lymph nodes before they start to proliferate. Given the dramatic effect of LIS1 on CD4+ T-cell proliferation at day 3, we anticipated that very low numbers of LIS1 deficient cells would survive at later time points after immunization. To address the reviewer’s comment, we transferred OT2+CD45.1+ CD4+ T cells stained with CTV in C57BL/6 mice and analyzed the percentages and numbers of CD45.1+ T cells as well as the dilution of CTV in those cells at day 7 after immunization. As expected, all CD45.1+ cells were negative for CTV at this time of analysis (data not shown). The percentages and numbers of CD45.1+ T cells were strongly decrease in the absence of LIS1 in comparison to wild-type controls (Figure 3 - Figure Supplement 2C), confirming results obtained at day 3 after immunization.

In the discussion, the authors speculate about the differences observed between CD4 and CD8 T cells, as the latter do now show proliferative defects upon TCR-triggered stimulation, and come up with the hypothesis that LIS1 might be important for symmetric cell divisions, but not for asymmetric cell divisions. However, the arguments used by the authors have few caveats, especially because CD4+ T cells can also undergo asymmetric cell division following TCR-triggered stimulation upon the first cognate antigen encounter (Chang et al., Science, 2007, Ref. 8).

We agree that CD4+ T cells can undergo asymmetric division (actually, this is mentioned and referenced p3 and p18 of the manuscript). However, it is unknown whether these divisions occur systematically or whether they occur with variable frequency which could be context-dependent. It is also unclear whether CD4+ and CD8+ T cells have similar rates of asymmetric division. The literature is lacking of comparative studies in which cellular events associated to mitosis would be investigated side-by-side in those two subsets. As mentioned to reviewer-1, only one study to our knowledge performed a comparative analysis of T-bet repartition in daughter cells after a first round of cell division in CD4+ and CD8+ T cells (Chang, J. T. et al., Immunity, 2011). They found that T-bet segregates unequally in daughter cells in both CD4+ and CD8+ T cells. However, the disparity between daughter cells was higher in CD8+ T cells as compared to that in CD4+ T cells (5- versus 3-fold). This suggests that key molecules are either more equally (or less unequally) distributed in daughter cells from the CD4+ lineage or that the rate of symmetric divisions is higher in CD4+ T cells than in the CD8+ T cells. Those results are in accordance with our interpretation and previous findings (Yingling, J. et al., Cell, 2008; Zimdahl, B. et al, Nature Genetics, 2014), suggesting that LIS1 is predominantly involved in mitosis associated to symmetric divisions. Another possibility to explain this difference is that asymmetrical division might occur at different stages in CD4+ and CD8+ T cells. Although some asymmetrical divisions have been detected early after antigen encounter in CD4+ T cells, a more recent study from the same group suggest that asymmetric division might occur mainly later after several rounds of divisions of CD4+ T cells to enable self-renewal to be coupled to production of differentiated effector CD4+ T cells (Nish, S. A., Journal of Experimental Medicine, 2017). It is therefore possible that LIS1 could be critical early in CD4+ T cell expansion, when cells mainly divide through symmetrical process, and less critical later when cells are engaged in asymmetrical division. This is now discussed in greater details p18 of the revised version of the manuscript.

Finally, the authors discuss that mono-allelic LIS1 defects might contribute to malignancies. Certainly not all points raised in the discussion need to be experimentally addressed, but for this particular hypothesis the authors would likely have the tools to achieve that, which would broaden the relevance of understanding LIS1 function.

We have addressed this point experimentally in the revised version of the manuscript. We show that mono-allelic LIS1 deficiency does not have a significant impact on the percentages of thymocyte populations in Cd2-Cre Lis1flox/+ mice (Figure 1 - Figure Supplement 1B) and on the numbers of peripheral T cells in Cd4-Cre Lis1flox/+ (Figure 3 - Figure Supplement 1E), suggesting that LIS1 does not operate in a dose-dependent fashion in the context of T-cell development and T-cell homeostatic maintenance. Additionally, Cd4-Cre Lis1flox/+ CD4+ T cells proliferate effectively following TCR and CD28 stimulation (Figure 3 - Figure Supplement 2A), indicating further that mono-allelic LIS1 dosage is sufficient to support cell division of CD4+ T cells. The part of the discussion related to Lis1 haplo-deficiency has been rephrased according to this new set of data.

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 #3 (Public Review):

In this paper, for the first time, metabolomics, proteomics, and lipidomics are combined to multi-dimensionally obtain more objective and scientific clues about early and advanced PMI, compared to the traditional methods of PMI estimation that relies on the subjective judgment of morphology. The "ForensOMICS" pipeline establishes a multi-omics analysis pipeline based on the LC-MS platform, which will bring influence and inspiration to the related research of PMI estimation based on molecular biological markers in the foreseeable future. However, due to the limitation of the availability of bone samples and metadata (which might contain covariates with latent influences on the PMI estimation), the current research is still a proof-of-concept study which is incomplete for the "ForensOMICS" approach to be applied in court.

Strengths:

Combing multiple omics and bioinformatics, as claimed by the authors, the "ForensOMICS" approach is more accurate and precise than the conventional morphological methods and molecular biological methods using single omics. Moreover, the research does not stop at developing time-dependent models using several omics biomarkers but carries on the enrichment analysis of relevant markers to further explore the pathophysiology mechanism behind the great changes in the internal environment after death, so as to provide meaningful reference data for the basic forensic research of death.

Data Integration Analysis for Biomarker discovery using Latent variable approaches for Omics studies (DIABLO) method and multiple features selecting tools are used in the bioinformatic process to analyze multiple omics data, and PMI classification model constructed based on PLS-DA, with parameters optimized by 3-fold/100 repeats cross-validation. The overall analysis process is relatively complete, and the data and classification model provided have scientific values for reference.

The "ForensOMICS" workflow in principle is compatible across metabolomics, proteomics, and lipidomics data obtained in different domains of proof-of-concept studies focusing on forensic-related time estimation (e.g. post-mortem submersion interval and time since deposit), for offering relatively complete analysis process.

Weaknesses:

Although the paper does have strengths in principle, the limitation of the availability of bone samples and metadata leads to the major weaknesses of the paper. Therein, age bias samples with single bone type and lack of analysis for environmental factors are the major weaknesses that argue against the key claims in the manuscript by the data presented.

The mean age of body donors is 74 years with {plus minus}11.6 years of standard deviation, while there was only one type of bone tissue (left anterior midshaft tibia). Different structures and locations of the sampled bone tissue as well as metabolic changes and bone degeneration caused by aging may lead to significant discrepancies in different multi-omics data. Moreover, most of the dead found at crime scenes are in the prime of life, and in addition to the tibia, other skeletal remains found at the scenes are commonly skull, ribs, upper limb bones, and teeth. Therefore, the relevant conclusions obtained from the research based on the limited bone samples cannot meet the actual needs for estimating the PMI of skeletal remains. As mentioned by the authors in the discussion, due to the difficulty in acquiring human remain samples with definite post-mortem intervals, this study is still proof-of-concept. If possible, the authors can focus on a larger sample set of different bone remains in younger age groups in future studies.

The reviewer is describing exactly the purpose of this manuscript. As highlighted by them, this paper is not intended to be an applicable method for PMI estimation at this stage, as we are aware of the differences that may exist between multiple skeletal elements and the omics results (at least, for proteomics data, as we published several papers on this topic). However, this is the proof of concept to demonstrate the potential that multiple omics combined together may have in addressing the PMI. We are committed to increase our sample size in order to develop a forensic technique for PMI estimation, that should anyway be then validated on multiple skeletal elements.

Tibia is frequently recovered from scenes also involving the presence of incomplete human remains subjected to long PMIs; our previous studies have also demonstrated that midshaft tibia may be an ideal candidate for proteomics analyses, due to its small intra-individual variability in comparison with other bones. Therefore, the selected sample for this pilot has been the anterior midshaft tibia. We do agree with the reviewer that such samples may not be representative of the whole bone proteome, metabolome, and lipidome composition (with particular regards to cortical and trabecular parts); however, this could be addressed as part of future studies on the topic.

We do agree with the reviewer about the possible confounding factor related to the relatively high variability in terms of age at death differences, that was indeed due to the difficult in acquiring human bodies with a known PMI.

Although in-life physiological and/or pathological conditions (i.e., osteoporosis) might be responsible for variability among baseline samples and between baseline and different long PMIs’ samples seen in several metabolites and proteins, we believe the biological phenomena underlying PMI are strong enough to overcome such limitations in the design of the experiment. This is also supported by the small inter-individual variability observed amongst the fresh/baseline samples.

It is suggested that metadata which may be influence factors of PMI such as temperature, humidity, UV-exposure, and deposition context (which is already recorded) should be recorded and statistically analyzed, so as to further optimize the "ForensOMICS" classification model by considering these possible environmental covariates. In addition, according to the No Free Lunch theorem, PLS-DA is very likely not to be the optimal solution for all the above-mentioned PMI classification tasks based on multi-omics data under different environmental conditions. It is recommended to develop and compare more different classification models for improving the generalization performance of the "ForensOMICS" approach.

We agree with the reviewer that these factors are crucial in the decomposition process. In our opinion, however, at this stage it is not appropriate to include these metadata in the statistical analysis as covariates by applying additional classification models, due to the small sample size available. Additionally, the main focus of the paper is exclusively on PMI-driven modifications. Environmental data have been added for reference in Supplementary File 2 and will be taken into account in future works when a bigger sample size will be evaluated.

Due to the limitation of sample size and the discrete-time gradients, the omics data obtained in the paper could only be applied to build a classification model rather than the regression model. Since such a model does not give a specific predicted PMI with MSE and RMSE indicating its performance, and the current "ForensOMICS" approach failed to distinguish different samples of late PMI (219-834 days), there is still a distance for "ForensOMICS" approach to apply in the actual forensic practice.

Thank you for your comments. We agree, and stressed across the whole manuscript, that this is far from being appliable to forensic practice. The proof-of-concept nature of the study represents a mandatory step for the building of a regression model than can be challenged in the future with the highly rigorous standard required in the forensic setting (i.e., Daubert criteria). We appreciate the understanding of the reviewer for the choice of modelling the data using classification rather than regression.

Author Response

Reviewer #1 (Public Review):

The authors define regulatory networks across 77 tissue contexts using software they have previously published (PECA2, Duren et al. 2020). Each regulatory network is a set of nodes (transcription factors (TF), target genes (TG), and regulatory elements (RE)) and edges (regulatory scores connecting the nodes). For each context, the authors define context-specific REs, as those that do not overlap REs from any of the other 76 contexts, and context-specific regulatory networks as the collection of TFs, TGs, and REs connected to at least one context-specific RE. This approach essentially creates annotations that are aggregated across genes, elements, and specific contexts. For each tissue, the authors use linkage disequilibrium score regression (LDSC) to calculate enrichment for complex trait heritability within the set of all REs from the corresponding context-specific regulatory network. Heritability enrichments in context-specific regulatory network REs are compared with heritability enrichments in regions defined using other approaches.

We thank the reviewers for the pertinent and precise summary of our paper.

Reviewer #2 (Public Review):

In this manuscript the authors develop a method, SpecVar, to perform heritability estimation from regulatory networks derived from gene expression and chromatin accessibility data. They apply this approach to public datasets available in ENCODE and Roadmap Epigenomics consortia as well as GWAS phenotype associations in UK Biobank. It promises to be a powerful method to interpret mechanisms from genetic associations. Below are some strengths and weaknesses of the paper.

Strengths

• The method performs heritability enrichment on two major genomic data types: gene expression and chromatin accessibility.

• This method leverages gene regulatory networks to perform the heritability estimation, which may better capture complex disease architecture.

• The authors perform an extensive comparison to other LDSC-based approaches using different tissue datasets.

Weaknesses

(1) This approach may represent a modest advance over existing LDSC methods when looking at other complex traits.

(2) The authors only compare with LDSC using different functional annotations as input, which may not be appropriate. A more broad comparison with other heritability methods would be helpful.

(3) The method seems to be applied to "paired" data, but this is still bulk profiles not paired single-cell RNA/ATAC data.

The authors successfully applied a regulatory network approach to improving the heritability estimation of complex traits by using both gene expression and chromatin accessibility data. While the results could be further strengthened by comparing them to other network and non-network-based methods, it provides important insight into a few traits beyond the standard LDSC model with different functional annotations.

Given that this method is based on the widely used LDSC approach it should be broadly applied in the field. However, the authors should consider adapting this to single-cell data as well as admixed human population genetic data.

We thank the reviewer for the positive comment on our work by specifically pointing out that SpecVar is a powerful method to interpret mechanisms from genetic associations. We appreciate that the reviewer’s summarized “Strength” part well captures our major contribution in building an atlas of regulatory networks by integrating paired gene expression and chromatin accessibility data, leveraging regulatory networks to perform the heritability enrichment, and identifying relevant tissues and estimate relevance correlation. We also thank the reviewer for pointing out the weakness to further enhance our results. To address the comments, we (1) performed ablation studies and added more description to clarify the novelty of our methods; (2) conducted extensive comparison to another network-based method CoCoNet and non-network-based method RolyPoly; (3) discussed the promising direction in identification of relevant contexts at cell type level by leveraging single cell multi-omics profiles and application on admixed populations.

Reviewer #3 (Public Review):

Identifying the critical tissues and cell types in which genetic variants exert their effects on complex traits is an important question that has attracted increasing attention. Feng et al propose a new method, SpecVar, to first construct context-specific regulatory networks by integrating tissue-specific chromatin states and gene expression data, and then run stratified LD score regression (LDSC) to test if the constructed regulatory network in tissue is significantly associated with the trait, measured by a statistic called trait relevance score in this study. They apply their method to 6 traits for which there exists prior evidence on the most relevant tissues in the literature, and then further apply to 206 traits in the UK Biobank. They find that compared to LDSC using other sources of information to define context-specific annotations, their method can "improve heritability enrichment", "accurately detect relevant tissues", helps to "interpret SNPs" identified from GWAS, and "better reveals shared heritability and regulations of phenotypes" between traits.

We thank the reviewer for the summary and appreciation of our efforts to address the important question: identifying the critical tissues and cell types in which genetic variants exert their effects on complex traits.

However, I think it requires more work to understand where exactly the benefits come from and the statistical properties of their proposed test statistic (e.g., how to perform hypothesis tests with their relevance score and whether the false positive rate is under control). In addition, it's not clear to me what they can conclude about the shared heritability (which means genetic correlation) by comparing their relevance score correlation across tissues to the phenotypic correlation between traits.

We thank the reviewer’s advice to do more work to enhance the statistical rigorousness of SpecVar. We have added the significant test of heritability enrichment and our proposed R score in the revision. We also clarified that SpecVar can use common relevant contexts and shared SNP-associated regulatory networks as potential explanation for the correlation between traits.

They show that SpecVar gives much higher heritability enrichment than the other methods in the trait-relevant tissues (Fig. 2). The fold enrichment from SpecVar is extremely high, e.g., more than 600x in the right lobe of the liver for LDL. First, I think a standard error should be given so that the significance of the differences can be assessed. Second, it is very rare (hence suspicious) to observe such a huge enrichment. Since SpecVar is based on LDSC, the same methodology that other methods in comparison depend on, the differences to the other methods must come from the set of SNPs annotated for each tissue. I think it is important to understand the difference between the SpecVar annotated SNPs and those from other methods. For example, is the extra heritability enrichment mainly from the SpecVar-specific annotation or from the intersection narrowed down by SpecVar?

The reviewer has pinpointed a question about one important advantage of our method to improve heritability enrichment. We addressed this question by first providing standard errors, p values, and q values of heritability enrichment. Second, we conduct the ablation analysis to study the source of extra heritability enrichment. This question greatly helps us to clarify the main contribution of our method.

They propose to use the relevance score (R score) to prioritise trait-relevant tissues. In Fig. 3, they show tissue-trait pairs with the highest R scores, and from there they prioritise several tissues for each trait (Table 1). I can see that some tissue has an outstanding R score, however, it is not clear to me where they draw the line to declare a positive result. The threshold doesn't seem to be even consistent across traits. For example, for LDL, only the right lobe of the liver is identified although other tissues have R scores greater than 100, whereas, for EA, Ammor's horn and adrenal gland are identified although their R scores are apparently smaller than 100. It seems to me they use some subjective criteria to pick the results. It leads to a serious question on how to apply their R score in a hypothesis test: how to measure the uncertainty of their R score? What significance threshold should be used? Whether the false positive rate is under control? (Without knowing these statistical properties, readers won't be able to use this method with confidence in their own research.

We thank the reviewer to raise the question about the hypothesis test of the R score. We used the block Jackknife stratagem to estimate standard errors, p values, and q values in our revision. We added the new result to the main text and they greatly enhanced the statistical rigorousness of our method.

Another related comment to the above is to investigate false positive associations, they should show the results for all tissues tested to see if SpecVar tends to give higher R scores even in tissues that are not relevant to the trait. It would also be useful to include some negative control traits, such as height for brain tissues.

We agree that negative control is important and the six phenotypes in our manuscript are negative for each other. For example, LDL is relevant to liver tissue and not relevant to brain tissue. Educational attainment is relevant to brain tissue but not relevant to liver tissue.

Fig. 3 shows that tissues prioritised by LDSC-SAP and LDSC-SEG seem to make less sense than those from SpecVar. However, some of the results are not consistent with the LDSC-SEG paper (Finucane et al 2018). For example, LDL was significantly associated with the liver in Finucane et al (Fig. 2), but not in this study. How to explain the difference? (Question 3)

We checked the results in Figure 3 and found that even though the liver was not ranked to be top 5 tissues, it has a significant P-value to LDL in our implementation. There is indeed some difference in heritability enrichment and P-value between the LDSC-SEG paper and our implementation. And the difference was from the different sets of tissues (77 tissues in our paper and 53 tissues in the LDSC-SEG paper) for the two applications.

The authors highlight an example where SpecVar facilitates the interpretation of GWAS signals near FOXC2. They find GWAS-significant SNPs located in a CNCC-specific RE downstream of FOXC2 and reason these SNPs affect brain shape by regulating the expression of FOXC2. I think more work can be done to consolidate the conclusion. For example, if the GWAS signals are colocalised with the eQTL for FOXC2 in the brain. Also, note that the top GWAS signal is actually on the left of the CNCC-specific RE (Fig. 4b). A deeper investigation should be warranted.

We agree that more work should be done to consolidate the regulation of FOXC2. In our revision, we used the HiChIP loop in the brain to support the SNP-associated regulation of FOXC2. We also thank the reviewer’s suggestion for the idea of eQTL colocalization and we conduct eQTL colocalization analysis on our method-revealed SNP-associated regulation to show our method can facilitate the fine mapping of GWAS signals. Lastly, brain shape is a complex trait and may be relevant to multiple tissues. Hence it is reasonable to suspect that the top GWAS signal may be active in other relevant tissues’ regulatory elements.

They show that SpecVar's relevance score correlation across tissues can better approximate phenotypic correlation between traits. However, the estimation of the phenotypic correlation between traits is neither very interesting nor a thing difficult to do (it can be directly estimated from GWAS summary statistics). A more interesting question is to which extent the observed phenotypic correlation is due to common genetic factors acting in the shared tissues/cell types/pathways/regulatory networks between traits. Note that in their Abstract, they use words "depict shared heritability and regulations" but I don't seem to see results supporting that.

We are sorry that we didn’t make it clear how SpecVar “depict shared heritability and regulations”. We added more results and one example in the UKBB application to show SpecVar can use common relevant contexts and shared SNP-associated regulatory networks as potential explanation for the correlation between traits.

Line 396-402: "For example, ... heritability could select most relevant tissues ... but failed to get correct tissues for other phenotypes ... P-value could obtain correct tissues for CP ... but failed to get correct tissues for ... SpecVar could prioritize correct relevant tissues for all the six phenotypes." Honestly, I find hard to judge which tissues are "correct" or "incorrect" for a trait in real life. It would be more straightforward to compare methods using simulation where we know which tissues are causal.

We thank the reviewers to pinpoint the improper statement of “correct”. It is difficult to find phenotypes with gold-standard relevant tissues and we used six relatively well-studied phenotypes with prior knowledge of possible relevant tissues in our paper. We revised the “correct” statement in our revision.

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.

References

1. Heyes, C. (2012). What’s social about social learning? Journal of Comparative Psychology 126, 193–202. 10.1037/a0025180.
2. Chang, S.W.C., and Dal Monte, O. (2018). Shining Light on Social Learning Circuits. Trends in Cognitive Sciences 22, 673–675. 10.1016/j.tics.2018.05.002.
3. Diaconescu, A.O., Mathys, C., Weber, L.A.E., Kasper, L., Mauer, J., and Stephan, K.E. (2017). Hierarchical prediction errors in midbrain and septum during social learning. Soc Cogn Affect Neurosci 12, 618–634. 10.1093/scan/nsw171.
4. Frith, C., and Frith, U. (2010). Learning from Others: Introduction to the Special Review Series on Social Neuroscience. Neuron 65, 739–743. 10.1016/j.neuron.2010.03.015.
5. Frith, C.D., and Frith, U. (2012). Mechanisms of Social Cognition. Annu. Rev. Psychol. 63, 287–313. 10.1146/annurev-psych-120710-100449.
6. Grabenhorst, F., and Schultz, W. (2021). Functions of primate amygdala neurons in economic decisions and social decision simulation. Behavioural Brain Research 409, 113318. 10.1016/j.bbr.2021.113318.
7. Lockwood, P.L., Apps, M.A.J., and Chang, S.W.C. (2020). Is There a ‘Social’ Brain? Implementations and Algorithms. Trends in Cognitive Sciences, S1364661320301686. 10.1016/j.tics.2020.06.011.
8. Soutschek, A., Ruff, C.C., Strombach, T., Kalenscher, T., and Tobler, P.N. (2016). Brain stimulation reveals crucial role of overcoming self-centeredness in self-control. Sci. Adv. 2, e1600992. 10.1126/sciadv.1600992.
9. Wittmann, M.K., Lockwood, P.L., and Rushworth, M.F.S. (2018). Neural Mechanisms of Social Cognition in Primates. Annu. Rev. Neurosci. 41, 99–118. 10.1146/annurev-neuro080317-061450.
10. Shafto, P., Goodman, N.D., and Frank, M.C. (2012). Learning From Others: The Consequences of Psychological Reasoning for Human Learning. Perspect Psychol Sci 7, 341– 351. 10.1177/1745691612448481.
11. McGuire, J.T., Nassar, M.R., Gold, J.I., and Kable, J.W. (2014). Functionally Dissociable Influences on Learning Rate in a Dynamic Environment. Neuron 84, 870–881. 10.1016/j.neuron.2014.10.013.
12. Behrens, T.E.J., Woolrich, M.W., Walton, M.E., and Rushworth, M.F.S. (2007). Learning the value of information in an uncertain world. Nature Neuroscience 10, 1214– 1221. 10.1038/nn1954.
13. Meder, D., Kolling, N., Verhagen, L., Wittmann, M.K., Scholl, J., Madsen, K.H., Hulme, O.J., Behrens, T.E.J., and Rushworth, M.F.S. (2017). Simultaneous representation of a spectrum of dynamically changing value estimates during decision making. Nat Commun 8, 1942. 10.1038/s41467-017-02169-w.
14. Allenmark, F., Müller, H.J., and Shi, Z. (2018). Inter-trial effects in visual pop-out search: Factorial comparison of Bayesian updating models. PLoS Comput Biol 14, e1006328. 10.1371/journal.pcbi.1006328.
15. Wittmann, M., Trudel, N., Trier, H.A., Klein-Flügge, M., Sel, A., Verhagen, L., and Rushworth, M.F.S. (2021). Causal manipulation of self-other mergence in the dorsomedial prefrontal cortex. Neuron.
16. Wittmann, M.K., Kolling, N., Faber, N.S., Scholl, J., Nelissen, N., and Rushworth, M.F.S. (2016). Self-Other Mergence in the Frontal Cortex during Cooperation and Competition. Neuron 91, 482–493. 10.1016/j.neuron.2016.06.022.
17. Kappes, A., Harvey, A.H., Lohrenz, T., Montague, P.R., and Sharot, T. (2020). Confirmation bias in the utilization of others’ opinion strength. Nat Neurosci 23, 130–137. 10.1038/s41593-019-0549-2.
18. Trudel, N., Scholl, J., Klein-Flügge, M.C., Fouragnan, E., Tankelevitch, L., Wittmann, M.K., and Rushworth, M.F.S. (2021). Polarity of uncertainty representation during exploration and exploitation in ventromedial prefrontal cortex. Nat Hum Behav. 10.1038/s41562-020-0929-3.
19. Yu, Z., Guindani, M., Grieco, S.F., Chen, L., Holmes, T.C., and Xu, X. (2022). Beyond t test and ANOVA: applications of mixed-effects models for more rigorous statistical analysis in neuroscience research. Neuron 110, 21–35. 10.1016/j.neuron.2021.10.030.
20. Mars, R.B., Jbabdi, S., Sallet, J., O’Reilly, J.X., Croxson, P.L., Olivier, E., Noonan, M.P., Bergmann, C., Mitchell, A.S., Baxter, M.G., et al. (2011). Diffusion-Weighted Imaging Tractography-Based Parcellation of the Human Parietal Cortex and Comparison with Human and Macaque Resting-State Functional Connectivity. Journal of Neuroscience 31, 4087– 4100. 10.1523/JNEUROSCI.5102-10.2011.
21. Yu, A.J., and Cohen, J.D. Sequential effects: Superstition or rational behavior? 8.
22. Nili, H., Wingfield, C., Walther, A., Su, L., Marslen-Wilson, W., and Kriegeskorte, N. (2014). A Toolbox for Representational Similarity Analysis. PLoS Comput Biol 10, e1003553. 10.1371/journal.pcbi.1003553.
23. Lockwood, P.L., Wittmann, M.K., Nili, H., Matsumoto-Ryan, M., Abdurahman, A., Cutler, J., Husain, M., and Apps, M.A.J. (2022). Distinct neural representations for prosocial and self-benefiting effort. Current Biology 32, 4172-4185.e7. 10.1016/j.cub.2022.08.010.

Author Response

Reviewer #1 (Public Review):

The authors performed simultaneous extracellular recordings in brain regions (CA1, prefrontal cortex (PFC), olfactory bulb (OB)) that are key to odor-guided decision making to delineate the oscillatory and cell population dynamics that guide decision making based on learned associations. They used complementary analyses to assess the coordination between CA1 and medial PFC (mPFC), using coherence and phase-locking analysis as well as generalized linear models and Bayesian decoding methods.

One of the strengths of this work is the comparison of beta and respiratory (RR) LFP coherence in several behavioral states to rule out confounds due to sniffing or preparatory motor behavior (e.g., coherence was assessed during decision making with and without an odor present, during reward consumption). These controls allowed the authors to identify a specific enhancement of beta compared to RR coherence during decision making.

The analyses of task-responsive putative interneuron and pyramidal cells suggest that accurate decision-making is associated with a stronger modulation of beta phase-locking in interneurons. Additional cross-correlation analyses between cell types across regions showed that cells, particularly interneurons, are temporally coordinated in the beta range. Their analyses did not identify a mechanism for this coordination, but the temporal lags between PFC and CA1 cells raise the possibility of top-down interactions mediated by a third brain region.

The authors used the cellular activity to determine that the animal's upcoming behavior could be predicted from the ensemble activity during decision-making a few hundred milliseconds before the behavioral choice, but decoding accuracy diminished soon after the decision-making period. Interestingly, decoding accuracy increased after decision-making when using the spatially active cell ensembles. As indicated by the authors, these results suggest that different cell ensembles are engaged during decision-making and during the execution of the decision. It is possible that this change in ensemble dynamics before and after decision-making relates to the familiarity of the animals with the task, which makes it likely to involve procedural components (e.g., Jog et al., 1999). As pointed out by the authors in the discussion, several results have implications for the formation of associative memories and provide clues for future experiments. Thus, future work looking at the ensemble dynamics and at the occurrence of CA1 ripples in the early stages of task learning compared to when the animals are very familiar with the task (as in the current study), will provide a better understanding of the shifts that develop during the formation and consolidation of the association.

One of the considerations in interpreting the results is that the odor sampling and decisionmaking periods overlap, making it difficult to disentangle the neural dynamics that are driven by the recall of the association (cued retrieval) and those that relate to the upcoming turning behavior after odor port disengagement. However, the author's analyses of odor and choice selectivity in correct and incorrect trials demonstrate a preferential association between spike activity and choice selection in this task.

Overall, the results advance our understanding of odor-guided decision-making mechanisms in CA1 and PFC at the LFP and cell population level. This work will be of significance to further research on the cellular basis of memory-guided decision-making, and to future work characterizing the interactions between CA1 and PFC during learning.

We thank the Reviewer for their detailed evaluation summarizing and highlighting the strengths of the study. In addition to beta and respiratory rhythm (RR) modulation of CA1-PFC activity and the relationship between spiking activity and choice selection, the Reviewer also highlighted the temporal coordination of CA1 interneurons and change in ensemble dynamics during the decision-making period at the odor-port vs. during the execution of the decision on the maze, which is further emphasized as a novel result in the revised manuscript.

Reviewer #2 (Public Review):

Symanski et al. investigated the communication between the medial prefrontal cortex (mPFC), the hippocampal CA1 region, and the olfactory bulb (OB) while rats underwent an odor-cued decision-making task. By recording local field potentials and spiking activity in the three regions, they found that all regions became synchronized at the beta band and respiratory rhythms during cue sampling/decision-making. Although the strength of inter-region synchrony was not predictive of correct choices, both CA1 and mPFC neurons showed stronger phase-locked firings to beta oscillations for correct than incorrect choices. Moreover, a subset of putative pyramidal and interneurons in both regions were selective for task variables, and as ensembles, they formed activity patterns differentiating choices. Also, their firings were temporally coordinated in a direction that the mPFC interneurons led CA1 interneurons and pyramidal neurons. Based on these findings, the authors propose that cue-evoked beta oscillations modulate the activity of interneurons to coordinate ensemble activity in CA1-mPFC networks supporting decision-making.

Strength:

The findings uncovered a new style of mPFC-Hippocampal communication through odorevoked beta oscillations, which contrasts with theta oscillations and sharp-wave/ripples reported during memory-guided spatial navigation tasks. The overall quality of the work is outstanding. The data collection and analysis were meticulously conducted with appropriate controls and statistical tests.

Weakness:

The initial analysis of LFP activity (Figure 2d) revealed strong coherence in the beta band in all region pairs; however, the subsequent analysis focuses on mPFC-CA1 interaction. To justify this approach, it is essential to establish that the mPFC-CA1 beta synchrony reflects their direct communication rather than a by-product of common inputs from the OB.

The authors used cross-correlograms to reveal the directionality of mPFC-CA1 interaction. To strengthen the author's view that beta oscillations help coordinate neural activity, it is worth investigating if the same temporal relationship is also detectable within each cycle of beta oscillations. Specifically, mPFC interneurons may fire at earlier phases, followed by firings of CA1 interneurons and pyramidal neurons at later phases.

We thank the Reviewer for their positive evaluation and constructive comments. We have addressed the weaknesses noted in the revised manuscript. In particular, we have added analyses and text that emphasize the change in beta synchrony in the OB-CA1PFC network during the task, and added analyses that examine phase locking of pyramidal cells and interneurons to beta rhythms in the mPFC, CA1 and OB.

Reviewer #3 (Public Review):

Symanski et al. describe a set of interesting results derived from analyzing electrophysiological recordings performed in rats well trained on an associative memory task on a spatial maze (a T maze), in which animals learned to associate a given odor delivered in an initial maze region (upon a nose poke) with a subsequent spatial choice (a left or a right turn) to receive a reward. The authors have obtained LFPs from the OB, PFC, and CA1 from 8 animals subjected to this task, along with single-unit activity from the PFC and CA1. The authors describe that, during odor sampling, there is prominent LFP activity in the beta range (20-30 Hz) as well as prominent activity of the respiration-entrained LFP rhythm (RR, 7-8 Hz). The authors convincingly show that beta activity - but not RR - is specific to odor sampling (RR also shows up during other immobility periods within the task and when animals breathed clean air). They further show that not only beta power but also inter-regional beta coherence significantly enhances during the odor sampling period. In addition, the authors find a higher beta phase modulation of spiking in a subset of neurons associated with subsequent correct decisions. Since the authors also prove - based on behavioral analysis - that the odor-sampling period corresponds to the decisionmaking period in this task, they propose a role for beta coordination of hippocampal-prefrontal networks in sensory-cued decision making. The paper also brings along a set of complementary findings looking at the single unit and ensemble activity in both regions (CA1 and PFC), which are capable of predicting future spatial choices.

I consider the investigated topic relevant to modern neuroscience and likely to interest a broad audience. Nevertheless, while there is much to like about this paper (e.g., carefully done experiments, advanced computational data analyses, well-written text, and well-crafted figures), I caught some issues that called my attention upon a careful reading, which I list below:

A) The paper is written in a way clearly centered on rhymical brain activity (c.f. title, abstract, introduction, and discussion). Yet, out of 7 main figures, only 2 of them show data related to oscillations (while 1 figure shows behavioral data and 4 figures show spiking analysis not related to brain rhythms). Therefore, the presentation of the results seems unbalanced and disconnected from the main story.

B) Somewhat related to the point above, in a strict sense, the title is not well justified ("Rhythmic coordination of hippocampal-prefrontal ensembles (...)") since there is no analysis relating assembly activity with either beta or RR (their results show beta or RR modulating a subset of single units), nor there is a combined ensemble analysis of PFC and hippocampal units (i.e., interregional cell assemblies). Why not try to relate ensemble activity to the observed oscillations?

C) The main result of increased interregional beta coherence specifically during odor sampling is very interesting and seems quite solid. Though I hate being the one raising questions about the level of advancement, I cannot avoid noticing that similar increases in beta coherence in odor-sampling-based tasks have been observed before (e.g., increased OB-HPC beta coherence during odor sampling has been shown in Martin et al 2007 and between LEC and HPC in Igarashi et al 2014), which is to say that there is overlap between this core finding and previous research. But that said, in times where the reproducibility of our scientific endeavor has been put into question, this particular reviewer favors the publication of similar findings by independent labs, especially given this neatly collected dataset. It is recommended to highlight which results constitute novel insights here and which results provide support for previously published results.

D) It called to my attention that many of the spiking results were obtained for a small percentage of neurons. For instance, how can the authors be confident that the choice-selective neurons are actually coding for the choice as opposed to being randomly detected by statistical chance? As a case in point, the authors mention that 1309 units were recorded in CA1, and from these 42 cells were choice selective. If the authors have employed a typical alpha of 5% for detecting such neurons, chance alone would predict ~60 neurons being false positives. I apologize if I am missing something, but could the authors clarify? On a related note, even though most findings hold true for a small percentage of neurons, the writing also tends to generalize the findings to the whole population (e.g., "Beta phase modulation of CA1 and PFC neuronal activity during this period was linked to accurate decisions, suggesting that this temporal modulation influences sensory-cued decision making.").

We thank the Reviewer for their detailed comments and feedback. We have addressed the issues raised by the Reviewer, which has significantly strengthened the manuscript.

A) We have added several new analyses for rhythmic modulation of spiking activity, and elevated some of the Supplementary Figures related to oscillations to the main figures (Figures 2, 5). In addition, since several of our analyses provide novel results for spiking and ensemble dynamics before and after the decision making period, as noted by Reviewer 1, and we have emphasized these results as a novel advance in the revised manuscript , including the title and abstract.

B) We agree that our analysis focuses on rhythmic coordination by beta and RR oscillations, phase modulation of single cell spiking activity in CA1 and PFC for accurate odor-cued decision making, and ensemble dynamics during decision making and execution of decisions. While relating ensemble activity to the observed oscillations is a long-term goal, we are limited by the size of simultaneously recorded ensembles within single sessions, since measures of ensemble dynamics per trial are required for such analyses. This is now noted in the Discussion section. We therefore focus our analyses separately on single cell modulation by rhythms and dynamics of ensemble activity during decision making.

We have also retitled the manuscript to indicate this: “Rhythmic coordination and ensemble dynamics in the hippocampal-prefrontal network for odor-place associative memory and decision making”, to more accurately reflect our results.

C) We appreciate the Reviewer’s favorable view on independent confirmation of previous results on beta coherence using our strong dataset. We have referenced previous results on OB-HPC, LEC-HPC and striatal beta coherence in the manuscript (e.g., Kay and Beshel 2010; Igarashi et al. 2014; Rangel et al. 2016; Leventhal et al., 2012).

In addition, we also highlight the novelty of our results in the manuscript, as noted by Reviewers 1 and 2. Our findings in these specific circuits, namely the PFC-CA1 network, during odor-cued decision making are novel. Our results show that beta phase modulation of a sub-population of phase-coherent CA1 and PFC neurons is linked to accurate decision making, elucidate selectivity and ensemble dynamics in these regions during decision making, and show that independent ensembles are recruited during odor-sampling vs. the execution of decisions on the spatial maze. These results are emphasized in the revised manuscript.

D) We apologize for the misunderstanding regarding the number of neurons. We had initially reported total number of neurons recorded across run and sleep sessions, including those with very few spikes during the task. In determining task-responsive and task-unresponsive neurons (Figure 3), the task-unresponsive set also includes a very large fraction of neurons that did not have sufficient spikes during the odor-sampling or decision making period (e.g. using a criterion of number of spikes equal to number of trials; similar numbers are seen with other criterion such as an absolute minimum number of spikes). These neurons should be more accurately denoted as “Odor Period Inactive”. Therefore a more accurate estimate of task-responsive neurons in CA1 and PFC indicating their task engagement is now shown in Figure 3, starting with neurons that had sufficient spikes for this analysis. Using this metric, a large fractions of neurons are task responsive and selective, similar to previously reported fractions in other studies (Igarashi, et al., 2014). We have added this description and numbers in the text (page 11 lines 230-241) and Methods (page 37 lines 795-797).

We have also toned down the interpretation by avoiding generalizing to the whole population, and note that beta phase modulation of phase-locked neurons is related to behavior accuracy. Here, in particular, our results suggest a key role of CA1 interneurons in beta-mediated interactions.

Author Response

Reviewer #2 (Public Review):

Reinforcement learning (RL) theory is important because it provides a broad, mathematically proven framework for linking behavioral states to behavioral actions, and has the potential for linking realistic biological network dynamics to behavior. The most detailed neurophysiological modeling uses biophysical compartmental models with the theoretical framework of HodgkinHuxley and Rall to describe the dynamics of real neurons, but those models are extremely difficult to link to behavioral output. RL provides a theoretical framework that could help bridge across the still-underexplored chasm between behavioral modeling and neurophysiological detail.

On the positive side, this paper uses a network of interacting neurons in region CA3 and CA1 (as used in previous models by McNaughton and Morris, 1987; Hasselmo and Schnell, 1994; Treves and Rolls, 1994; Mehta, Quirk and Wilson. 2000; Hasselmo, Bodelon and Wyble, 2002) to address how a simple representation of biological network dynamics could generate the successor representation used in RL. The successor representation is an interesting theory of hippocampal function, as it contrasts with a previous idea of model-based planning. Previous neuroscience data supports the idea that animals use a model-based representation (a cognitive map made up of place cells or grid cells) to read out potential future paths to plan their behavior in the environment. For example, Johnson and Redish, 2007 showed activity spreading into alternating arms of a T-maze before a decision is made (i.e. a model-based exploration of possible actions, NOT a successor representation), and Pfeiffer and Foster, 2013 showed that replay in 2-dimensions corresponds to future goal directed activity. Models such as Erdem and Hasselmo, 2012 and Fenton and Kubie, 2012 showed how forward planning of possible trajectories could guide performance of behavioral tasks. In contrast, the successor representation proposes that model-based activity is too computationally expensive and proposes that instead of reading out various possible model-based future paths when making a decision, that a simulated agent could instead learn a look-up table indicating the probability of future behavioral states accessible from a given state. In previous work, the successor representations accounted for certain aspects of experimental neuroscience data such as place cells responding to the insertion of barriers as seen by Alvernhe et al. and the backward expansion of place field seen by Mehta et al. The current paper is admirable for addressing the potential role of neural replay in training of successor representations and its relationship to other neural and behavioral data such as the papers by Cheng and Frank 2008 and by Wu et al. 2017.

However, a lot of this same data could still be interpreted as indicating that animals use a model-based representation as described above. There's nothing in this paper that rules out a model-based interpretation of the results discussed above. In fact, the cited paper by Momennejad et al. 2017 shows that humans extensively use model-based mechanisms along with some use of a successor representation in addition to the model-based mechanism. The description in the article under review needs to avoid treating successor representations as if they are already the ground truth.

To do this, throughout the paper, the authors need to repeatedly address the fact that the Successor Representation is just a theory and not proven experimental fact. And they need to repeatedly in all sections point out that the successor representations hypothesis can be contrasted with the theory that model-based neural activity could instead guide behavior and could be the correct account for all of the data that they address (i.e. such as the darkavoidance behavior). They should cite the previous examples of neural data that looks like model-based planning such as Johnson and Redish, 2007 in the T-maze and Pfeiffer and Foster, 2013 in open fields, and cite models such as Hasselmo and Eichenbaum, 2005; Erdem and Hasselmo, 2012 and Fenton and Kubie, 2012 that showed how forward replay or planning of possible trajectories could guide performance of behavioral tasks

We thank the reviewer for the valuable feedback. We have adapted the manuscript throughout to discuss the important point that the SR is not the ground truth (e.g. the final paragraphs in the sections “Bias-variance trade-off” and “Leveraging replays to learn novel trajectories”). We also discussed more extensively the model-based literature and the suggested citations in the manuscript.

The title and text repeatedly refers to a "spiking" model. They show spikes in Figure 2 and extensively discuss the influence of spiking on STDP, but they ought to more explicitly discuss the interaction of their spike generation mechanisms (using a Poisson process) and the authors should compare their model to the model of George, DeCothi, Stachenfeld and Barry which addresses many of the same questions but using theta phase precession to obtain the correct spike timing in STDP.

Yes, that's a great suggestion. We have extended our discussion section. In particular, we added:

In our work, we did not include theta modulation, but phase precession and theta sequences could be yet another type of activity within the TD lambda framework. Interestingly, more groups have recently investigated related ideas. A recent work \citep{George2022} incorporated the theta sweeps into behavioural activity, showing it approximately learns the SR. Moreover, theta sequences allow for fast learning, playing a similar role as replays (or any other fast temporalcode sequences) in our work. By simulating the temporally compressed and precise theta sequences, their model also reconciles the learning over behavioral timescales with STDP. In contrast, our framework reconciles both timescales relying purely on rate-coding during behaviour. Finally, their method allows to learn the SR within continuous space. It would be interesting to investigate whether these methods co-exist in the hippocampus and other brain areas. Furthermore, \citep{Fang2022} et al. recently showed how the SR can be learned using recurrent neural networks with biologically plausible plasticity.

The introduction and start of the Results section are should have more citations to neuroscience data. The introduction currently cites only three experimental citations (O'Keefe and Dostrovsky, 1971; O'Keefe and Nadel, 1978 and Mehta et al. 2000) and then gives repeated citations of previous theory papers as if those papers define the experimental data that is relevant to this study. The article should review actual neuroscience literature, instead of acting as if a few theory papers in the last five years are more important sources of data than decades worth of experimental work. The start of the results section makes a statement about the role of hippocampus and only cites Stachenfeld et al. 2017 as if it were an experimental paper. The introduction, start of results and discussion need to be modified to address actual experimental data instead of just prior modeling papers. They need to add at least a paragraph to the introduction discussing real experimental data. There are numerous original research papers that should be cited for the role of hippocampus in behavior so that the reader doesn't get the impression all of this work started with the paper by Stachenfeld et al. 2017. For example, the introduction should supplement the citations to O'Keefe and Mehta with other experimental papers including those that they cite later in the paper. They should also cite other seminal work of Morris et al. 1982 in Morris water maze and Olton, 1979 in 8-arm radial maze and work by Wood, Dudchenko, Robitsek and Eichenbaum on neural activity during spatial alternation. At the start of the Results, instead of only citing Stachenfeld (which should have reduced emphasis when speaking about experiments), they should again cite O'Keefe and Nadel, 1978 for the very comprehensive review of the literature up to that time, plus the work of Morris and Eichenbaum and Aggleton and other experimental work.

We thank the reviewer for the suggested citations. We have added many citations in order to discuss the experimental literature more thoroughly.

This article is admirable for addressing how to utilize a continuous representation of space and time, which Kenji Doya also addressed in his NeurIPS article in 1995 and Neural Computation 2000 (which should be cited). To emphasize the significance of this continuous representation, they could note that reinforcement learning (RL) theory models still tend to use a discretized grid-like map of the world and discrete representation of time that does not correspond to the probabilistic nature of place cell response properties (Fenton and Muller) and the continuous nature of the response of time cells (Kraus et al. 2013).

We thank the reviewer for this important comment and this is indeed one of the main strengths of the proposed framework. We have now emphasised this point, by adding the following paragraph to the Discussion:

“Importantly, the discount parameter also depends on the time spent in each state. This eliminates the need for time discretization, which does not reflect the continuous nature of the response of time cells (Kraus et al. 2013).”

I think the authors of this article need to be clear about the shortcomings of RL. They should devote some space in the discussion to noting neuroscience data that has not been addressed yet. They could note that most components of their RL framework are still implemented as algorithms rather than neural models. They could note that most RL models usually don't have neurons of any kind in them and that their own model only uses neurons to represent state and successor representations, without representing actions or action selection processes. They could note that the agents in most RL models commonly learn about barriers by needing to bang into the barrier in every location, rather than learning to look at it from a distance. The ultimate goal of research such as this should to link cellular level neurophysiological data to experimental data on behavior. To the extent possible, they should focus on how they link neurophysiological data at the cellular level to spatial behavior and the unit responses of place cells in behaving animals, rather than basing the validity of their work on the assumption that the successor representation is correct.

We thank the reviewer for this suggestion, we have now extended the Discussion to include a paragraph on the “Limitations of the Reinforcement Learning framework” which we reproduce here:

We have already outlined some of the perks of using reinforcement learning for modelling behaviour, including providing clear computational and algorithmic frameworks. However, there are several intrinsic limitations to this framework. For example, it needs to be noted that RL agents that only use spatial data do not provide complete descriptions of behavior, which likely arises from integrating information across multiple sensory inputs. Whereas an animal would be able to smell and see a reward from a certain distance, an agent exploring the environment would only be able to discover it when randomly visiting the exact reward location. Furthermore, the framework rests on fairly strict mathematical assumptions: typically the state space needs to be markovian, time and space need to be discretized (which we manage to evade in this particular framework) and the discounting needs to follow an exponential decay. These assumptions are overly simplistic and it is not clear how often they are actually met. Reinforcement Learning is also a sample-intensive technique, whereas we know that some animals, including humans, are capable of much faster or even one-shot learning. \ Regarding the specific limitations of our model, we can note that even though we have provided a neural implementation of the SR, and of the value function as its read-out (see Figure 5-figure supplement S2, the whole action selection process is still computed only at the algorithmic level. It may be interesting to extend the neural implementation to the policy selection mechanism in the future.

Author Response

Reviewer #2 (Public Review):

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

Strengths:

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

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

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

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

We appreciate his recognition of the quality of our research.

Weaknesses:

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

Why mNAMPT:

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

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

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

In the results, we changed the text accordingly:

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

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

In Materials and methods, we added a new section:

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

We also updated the results referencing it.

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

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

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

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

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

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

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

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

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

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

Author Response

Reviewer #1 (Public Review):

Alexander Komkov et al. developed a novel software/algorithm (iROAR) to utilise naturally occurring non-functional clonotypes as a control repertoire to correct for amplification bias associated with multiplex PCR based technologies commonly used in TCR/BCR repertoire analysis. No new data was generated in this study and utilises only publicly available datasets. The authors firstly determine the over amplification rate (OAR) as a metric which is found to be close to 1 under no or little amplification bias and this was validated by calculating the OAR for repertoires determined using 5'-RACE, a method known to have little to no amplification bias. This was a great control to have and is essential for validating the OAR measurement. In contrast, multiplex PCR based protocols such as VMPlex and VJMplex had significant deviations in the distribution of OAR.

Strengths: The authors used publicly available datasets that utilise both biased (multiplex PCR based) and low biased (5'-RACE) methods to determine TCR/BCR repertoires. In addition, the authors generated in silico biased 5'-RACE datasets. These comparisons are critical in determining the effect of bias correction.

Weaknesses: Analysis of TCR/BCR repertoires are very generalised to number of clonotypes. The use of this algorithm could be more widespread if the effect of iROAR on another repertoire analysis tools was determined or discussed. For example, does iROAR affect measures of diversity? Identification of rare but unique clonotypes? The ability to detect true clonal expansions? Additionally, documentation for the software is lacking and largely inaccessible to non-specialists.

By default, iROAR does not affect diversity and does not remove any clones. This statement was added to the manuscript. For now, the analysis of the potential effect on the detection of true clonal expansion is infeasible due to the lack of appropriate data with sufficient sequencing coverage. Also, we’ve made a more detailed description of iROAR software.

Reviewer #2 (Public Review):

In this paper, Komkov et al. describe a novel approach for computational correction of PCR amplification bias in adaptive immune receptor repertoire (AIRR) sequencing data (AIRR-seq). Their correction algorithm is based on using out-of-frame rearrangements to approximate gene-specific amplification bias. Gene-specific relative frequencies among out-of-frame rearrangements are not altered by clonal expansion except to the extent that out-of-frame rearrangements are passengers in clones expanding as a consequence of the specificity of the functional rearrangement. Due to independence between the two rearrangements, it can be reasonably assumed that the effects of clonal expansion are uniform in their impact on the observed V- and J-gene frequencies among out-of-frame rearrangements. Komkov et al. further assume that gene-specific relative frequencies among unique, out-of-frame rearrangements approximate recombination frequencies and that the extent to which gene-specific relative frequencies among all out-of-frame rearrangements deviate from those among unique, out-of-from rearrangements provides an estimate of gene-specific PCR amplification bias. The ratio of V- or J-gene relative frequencies among all out-of-frame rearrangements to the corresponding relative frequency among unique out-of-frame rearrangements provides this estimate and can be used as a correction factor during data processing. It also serves as the basis for a repertoire-level metric of the overall extent of amplification bias in a repertoire.

This is a very nice and, to the best of my knowledge, novel idea. The proposed correction factor and metric have potential utility in all studies conducting AIRR-seq that use a PCR amplification step. While the proposed approach may not have superior or even equal performance when compared to biological spike-ins, it still has great potential utility given the time and financial costs and required expertise of using biological spike-ins and because it can be applied to data sets that have already been generated. Incorporation of this approach into AIRR-seq data processing has the potential to increase the accuracy of downstream analyses. It also has the potential to enhance the comparability of results across studies and to reduce the effects of different sequencing protocols for data re-use when data are integrated across studies.

Enthusiasm is dampened by the fact that the proposed method is not directly compared to the gold standard of biological spike-ins.

During manuscript revision, we designed and performed an additional wet-lab experiment to directly compare the iROAR approach with biological spike-ins.

Author Response

Reviewer #1 (Public Review):

This manuscript describes the generation and characterization of a mouse knockout model of Cep78, which codes for a centrosomal protein previously implicated in cone-rod dystrophy (CRD) and hearing loss in humans. Previous work in cultured mammalian cells (including patient fibroblasts) also indicated roles for CEP78 in primary cilium assembly and length control, but so far no animal models for CEP78 were described. Here, the authors first use CRISPR/Cas9 to knock out Cep78 in the mouse and convincingly demonstrate loss of CEP78 protein in lysates of retina and testis of Cep78-/- animals. Next, by careful phenotypic analysis, the authors demonstrate significant defects in photoreceptor structure and function in these mutant animals, which become more severe over a 9 (or 18) month period. Specifically, TEM analysis demonstrates ultrastructural defects of the connecting cilium and photoreceptor outer segments in the Cep78 mutants, which is in line with previously reported roles for CEP78 in CRD and in regulating primary cilia assembly in humans. In addition to a CRD-like phenotype, the authors also convincingly show that male Cep78-/- animals are infertile and exhibit severe defects in spermatogenesis, sperm flagella structure and manchette formation (MMAF phenotype). Furthermore, the authors provide evidence for an MMAF phenotype from a male individual carrying a previously reported CEP78 c.1629-2A>G mutation, substantiating that CEP78 is required for sperm development and function in mammals and supporting previously published work (Ascari et al. 2020).

Finally, to identify the underlying molecular mechanism by which CEP78 loss causes MMAF, the authors perform some biochemical analyses, which suggest that CEP78 physically interacts with IFT20 and TTC21A (an ortholog of Chlamydomonas IFT139) and might regulate their stability. The authors conclude that CEP78 directly binds IFT20 and TTC21A in a trimeric complex and that disruption of this complex underlies the MMAF phenotype observed in Cep78-/- male mice. However, this conclusion is not fully justified by the data provided, and the mechanism by which CEP78 affects spermatogenesis therefore remains to be clarified.

Specific strengths are weaknesses of the manuscript are listed below.

Strengths:

Overall, the phenotypic characterisation of the Cep78-/- animals appears convincing and provides new evidence supporting that CEP78 plays an important role in the development and function of photoreceptors and sperm cells in vertebrates.

Weaknesses:

1) The immunoprecipitation experiments of mouse testis extracts that were used for the mass spectrometry analysis in Table S4 were performed with an antibody against endogenous CEP78 (although antibody details are missing). One caveat with this approach is that the antibody might block binding of CEP78 to some of its interactors, e.g. if the epitope recognized by the antibody is located within one or more interactor binding sites in CEP78. This could explain why the authors did not identify some of the previously identified CEP78 interactors in their IP analysis, such as CEP76 and the EDD-DYRK2-DDB1-VprBP complex (Hossain et al. 2017) as well as CEP350 (Goncalves et al. 2021).

We thank Reviewer #1 (Public Review) for agreeing with us on Cep78 plays an important role in photoreceptors and sperm cells development. We also appreciate Reviewer #1 (Public Review) for pointing out the weaknesses which helped us improve our study.

For the immunoprecipitation experiments of mouse testis extracts, the antigenic sequence of the Cep78 antibody used is p457-741 (NP_932136.2). Cep78 was reported to bind DD-DYRK2-DDB1-VprBP complex, the 1-520aa is responsible for Cep78’s interaction with VprBP, and deletion of p450-497 didn’t affect Cep78’s interaction with VprBP, indicating importance of Cep78 (1-450aa) in interaction with VprBp (Hossain et al. 2017). Our anti-Cep78 antibody is generated using antigen sequence p457-741, the binding of p1-450aa to VprBP is not expected to be blocked by our anti-Cep78 antibody. However, VprBp was not detected by our IP-MS experiment. C-terminal region (395-722aa) of Cep78 overlaps with our Cep78 antibody’s antigenic region (p457-741), and was reported to interact with Cep350 (Goncalves et al. 2021). As a polyclonal antibody, our anti-Cep78 antibody didn’t block the interaction with p457-741, because we still identified Cep350 in our IP-MS. Thus, immunoprecipitation experiments using our Cep78 antibody identified some of the previously known interactors, and the interaction with VprBP may not be blocked by our Cep78 antibody.

The detailed antibody information has now been added to Supplementary Table S7 in our revised supplementary materials.

2) Figure 7A-D and page 18-25: based on IPs performed on cell or tissue lysates the authors conclude that CEP78 directly binds IFT20 and TTC21A in a "trimeric complex". However, this conclusion is not justified by the data provided, nor by the previous studies that the authors are referring to (Liu et al. 2019 and Zhang et al. 2016). The reported interactions might just as well be indirect. Indeed, IFT20 is a known component of the IFT-B2 complex (Taschner et al., 2016) whereas TTC21A (IFT139) is part of the IFT-A complex, which suggests that they may interact indirectly. In addition, the IPs shown in Figure 7A-D are lacking negative controls that do not coIP with CEP78/IFT20/TTC21A. It is important to include such controls, especially since IFT20 and CEP78 are rich in coiled coils that tend to interact non-specifically with other proteins.

Thank Reviewer #1 (Public Review) for the comment on protein interaction between Cep78, Ift20, and Ttc21a. As the reviewer pointed out, IFT20 is a known component of the IFT-B2 complex (Taschner et al., 2016) whereas TTC21A (IFT139) is part of the IFT-A complex. Both IFT20 and TTC21a are located at peripheral areas of IFT-B and IFT-A (PMID: 32456460), and are not core components of IFT-A or IFT-B. It is still possible that these two proteins interact with each other. Actually, Liu et al. have revealed interaction between Ift20 and Ttc21a in human sperm (PMID: 30929735). Additionally, to mediate trafficking of ciliary axonemal components, the IFT machinery is recruited to the distal appendages (PMID: 30601682), which is adjacent to the distal end of the (mother) centriole wall, where at the (mother) centriole wall was reported to be located (PMID:35543806). Cep78 may interact with Ift20 and Ttc21a at centriole during cilliogenesis.s

To rule out the nonspecific interaction between Cep78 and Ttc21a or Ift20, we added additional negative controls of Gapdh (Figure 7D) and Ap80-NB-HA (Supplementary Figures S7A-C) in co-IP as the reviewer suggested, and found that the interaction between Cep78 and Ttc21a or Ift20 is specific. To examine if Cep78, Ift20 and Ttc21a formed a complex, we fractionated testicular protein complexes using size exclusion chromatography, and found that Cep78, Ift20 and Ttc21a co-fractioned at the size between158 kDa to 670 kDa (Figure 7E), supporting the formation of a trimeric complex. And our immunofluorescent analysis by SIM also showed co-localization between Cep78 and Ift20 or Ttc21a (Figure 7F). All these data support the interaction among Cep78, Ttc21a and Ift20. In the revised manuscript, we rephrased “direct interaction” as “interaction” at page 18, line 393 in the revised manuscript.

3) In Figure 7D, the input blots show similar levels of TTC21A and IFT20 in control and Cep78-/- mouse testicular tissue. This is in contrast to panels E-G in the same figure where TTC21A and IFT20 levels look reduced in the mutant. Please explain this discrepancy.

Thank you for pointing this out. Deletion of Cep78 caused down-regulation of Ttc21a and Ift20 proteins. To better reveal the change of interaction between Ttc21a and Ift20, we have to normalize their interaction against expression levels. To achieve this, we increased the amount of total Cep78-/- testicular proteins to ensure that Ttc21a and Ift20 in the input are at similar levels between Cep78+/- and Cep78-/- testes. Using 3 times the amount of the Cep78+/- testicular proteins for Cep78-/- testicular proteins, we detected similar protein levels of Ttc21a and Ift20 between Cep78-/- and Cep78+/- testes, and the interaction between Ttc21a and Ift20 was shown to be down-regulated after Cep78 deletion. Consistently, the analysis of GAPDH as a loading control in input proteins showed more Cep78-/- testicular proteins than Cep78+/- testicular proteins subjected to analysis. To avoid confusion, we have added description of “The amount of Cep78-/- testicular proteins used was 3 times of that of Cep78+/- proteins” in the legend of Figure 7D in the revised version of manuscript.

4) The efficiency of the siRNA knockdown shown in 7J-M was only assessed by qPCR (Figure S4), but this does not necessarily mean the corresponding proteins were depleted. Western blot analysis needs to be performed to show depletion at the protein level. Furthermore, it would be desirable with rescue experiments to validate the specificity of the siRNAs used.

Thank the reviewer for the suggestion. To validate the specificity of the siRNAs used, we performed rescue experiments using rescue plasmid with siRNA targeting sequence synonymously mutated (Supplementary Table S6). The efficiency of siRNA knockdown and effects of rescue experiments were evaluated by both qPCR (Supplementary Figures S4.A-C) and Western Blot (Figures 7.J-K, Supplementary Figures S4.D-E, H-I). The results showed that siRNAs significantly reduced the expression of Cep78, Ift20, and Ttc21a at both mRNA (Supplementary Figures S4.A-C) and protein levels (Figures 7.J-K, Supplementary Figure S4.A-C). Meanwhile, with siRNA treatment, the rescue plasmids rescued the expression of Cep78, Ift20, and Ttc21a at both mRNA (Supplementary Figures S4.A-C) and protein levels (Figures 7.J-K, Supplementary Figures S4.D-E, H-I) compared with the control groups.

In the rescue experiments, we further evaluated whether the effects are specific for Cep78, Ift20 and Ttc21siRNAs in the regulation of cilia and centriole lengths. The results showed that suppression of cilia and centriole lengths by Cep78, Ift20 and Ttc21siRNAs could be rescued by overexpression of rescue plasmids of Cep78syn-HA, Ift20syn-Flag and Ttc21asyn-Flag (Figures 7.N-S).

5) Figure 7I: the resolution of the IFM is not very high and certainly not sufficient to demonstrate that CEP78, IFT20 and TTC21A co-localize to the same region on the centrosome, which one would have expected if they directly interact.

Thank the reviewer for the constructive comments. To better demonstrate co-localization of CEP78, IFT20 and TTC21A on the centrosome, we overexpressed Cep78-Halo, Ift20-mCherry and Ttc21a-mEmerald in NIH3T3 cells by lentivirus, and acquired super-resolution images with SIM (N-sim, Nikon, Tokyo, Japan). The SIM results showed that Ift20 and Ttc21a co-localized with Cep78 (Figure 7F). Cep78 was previously reported to localize at the centriole (Goncalves et al., 2021). The co-localization of Cep78, Ift20 and Ttc21a indicated possible important roles of Cep78 in the regulation of Ift20 and Ttc21a in centriole. Our interaction analysis revealed that Cep78 interacted with Ift20 and Ttc21a (Figure 7A-C, Supplementary Figure S7), and formed a complex with Ift20 and Ttc21a (Figure 7E). Loss of Cep78 down-regulated the expression of and interaction between Ift20 and Ttc21a (Figures 7D, G-M).

6) It is not really clear what information the authors seek to obtain from the global proteomic analysis of elongating spermatids shown in Figure 3N, O and Tables S2 and S3. Also, in Table S2, why are the numbers for CEP78 in columns P, Q and R so high when Cep78 is knocked out in these spermatid lysates? Please clarify.

Thank the reviewer for the comments. Our global proteomic analysis showed that majority of differentially expressed proteins were down-regulated (Figure 3N), and many proteins are centrosome- and cilia-related proteins and important for sperm flagella and acrosome structures (Figure 3O), which provide insights of downstream molecular events in sperm flagella and acrosome defects after Cep78 deletion.

As to the quantification of CEP78 expression in TMT-based proteomics analysis, the ratio between Cep78-/- and Cep78+/- is relatively high due to the ratio compression effect, a well-known phenomenon in TMT-based proteomics analysis (PMID: 25337643). The actual difference in protein expression is usually higher than the ratio calculated by TMT signals. Actually, our Western blot analysis of CEP78 protein showed absence of expression in Cep78-/- testis. Although TMT labelling has the disadvantage of ratio compression (PMID: 32040177，PMID: 23969891), it is widely used quantitative proteomics analysis, and is demonstrated to be able to identify key pathways and proteins (PMID: 30683861, 33980814).

7) Figure 1F and Figure 4K: the data needs to be quantified.

Thank the reviewer for this suggestion. For Figure 4K, we stained Cep78+/- and Cep78-/- spermatids with anti-Centrin 1 to measure the centriole length. The statistical data of centriole length were provided (Figure 4L), showing significantly increased centriole lengths in Cep78-/-spermatids.

For Figure 1F, we quantified the immunofluorescence intensities of cone arrestin of light-adapted retinas of Cep78+/- and Cep78-/- mice at 3-month. The results indicate that immunofluorescence intensity of the cone arrestin was lower in Cep78-/- mice.

8) Figure 2A: It is difficult to see a difference in connecting cilium length in control and Cep78-/- mutant retinas based on the images shown here.

Thank you for your suggestion, we have stained retinal cryosections from Cep78+/- and Cep78-/- mice with anti-Nphp1 to visualize connecting cilium, and the data are provided in the revised Figure 2A-B.

Reviewer #2 (Public Review):

In this report, the authors have described the generation and characteristics of Cep78 mutant mice. Consistent with the phenotype observed in patients carrying the mutations in CEP78, Cep78 knock-out mice show degeneration in photoreceptors cells as well as defects in sperm. The author further shows the CEP78 protein can interact with IFT120 and TTC21a. Mutation in CEP78 results in a reduction of protein level of IFT120 and TTC21A and mislocalization of these two proteins, offering mechanistic insights into the sperm defects. Over all the manuscript is well written and easy to follow. Phenotyping is thorough. However, improvement of the background section is needed. In addition, some of the conclusion is not sufficiently supported by the data, warranting further analysis and/or additional experiments. The Cep78 KO mice model established by the author will be a useful model for further elucidating the disease mechanism in human and developing potential therapy.

My comments are the following:

1) Introduction. The statement that "CRD usually exists with combination of immotile cilia defects in other systems" is not correct. CRD due to ciliopathy can have cilia-related syndromic defects in other systems but it is a relatively small portion of all CRDs and the most frequently mutated genes are not cilia-related genes, such as ABCA4, GUCY2D, CRX.

Thank the reviewer for the comments. We agree with the reviewer that only a small portion of CRDs are due to cilia defects and can have cilia-related syndromic defects in other systems. We corrected this statement in Line 4, Page 77-79 of the revised version of our manuscript. In our revised version, the statement has been changed to “A small portion of CRDs are due to retina cilia defects, and they may have cilia-related syndromic defects in other systems[1].”

2) Introduction: Page 4 CNGB1 encodes channel protein and not a cilia gene. It should be removed since it does not fit.

Thank the reviewer for the comment. According to the reviewer’s suggestion, we removed the description of “mutations in CNGB1 cause CRD and anosmia [3]” at Page 4, Line 81 in the revised manuscript.

3) Page 5, given the previous report of CEP78 patients with retina degeneration, hearing loss, and reduced infertility, the statement of "we report CE79 as a NEW causative gene for a distinct syndrome...TWO phenotypes....." Is not accurate.

Thank the reviewer for the comments. We have removed the statement of “NEW” causative gene in Page 5, Line 104 of the revised version of our manuscript. The revised sentence is “In this study, based on results of a male patient carrying CEP78 mutation and Cep78 gene knockout mice, we report CEP78 as a causative gene for CRD and male sterility.”

4) Figure 1F, the OS of the cone seems shorter, which might be the reason for weaker arrestin staining in the mutant compared to the heterozygous. Also, it would be better to quantify the staining to substantiate the statement.

Thanks for this suggestion. For Figure 1F, we have quantified the immunofluorescence intensity of cone arrestin in Cep78+/- and Cep78-/- light-adapted retinas at 3-month. The results indicate that immunofluorescence intensity of the cone arrestin was significantly lower in Cep78-/- mice.

5) Figure 1K, panel with lower magnification would be useful to get a better sense of the overall structure defect of the retina. Is the defect observed in the cone as well?

Thank the reviewer for the comment. As suggested by the reviewer, we have provided images of lower magnification to show the overall structure by TEM, showing disruption of most outer segment in Cep78-/- retina. It is difficult to distinguish whether the disordered outer segment structure belongs to a cone or a rod cell. The images are now provided as Figure 1L in the revised manuscript.

We observed the abnormality of photopic b-wave amplitudes (Figure 1B, E) and decreased intensity of cone arrestin in light-adapted retinas (Figure 1F, G) in Cep78-/- mice, which indicate that the function of cone cells is damaged.

6) Figure 2A, NPHP1 or other markers specifically label CC would be more useful to quantify the length of CC. Also need to provide a notation for the red arrows in Figure 2. In addition, the shape of CC in the mutant seems differ significantly from the control. It seems disorganized and swollen.

Thank the reviewer for the suggestion. According to the reviewer’s suggestion, we have stained anti-Nphp1 in retinal cryosections from Cep78+/- and Cep78-/- mice to visualize connecting cilium, and quantified the length of CC. The results showed that connecting cilia were shorter in Cep78-/- mice. These data are showed in Figure 2A-B.

Besides, we observed that upper parts of connecting cilia were swelled with disorganized microtubules in TEM (Figure 2E-G). The red arrows in Figure 2E-G indicated swelled upper part of connecting cilia and disorganized microtubules of Cep78-/- photphoreceptors, we added this description in the figure legend.

7) Evidence provided can only indicate direct interaction among CEP78/IFT20/TTC21A.

Thanks for the comment. To further validate the interaction between Cep78 and Ttc21a or Ift20, we performed reciprocal co-IP between Cep78 and Ttc21a or Ift20 by overexpression (Figure 7A-C), and also added relevant negative control of Gapdh (Figure 7D) and Ap80-NB-HA (Supplementary Figures S7A-C) in co-IP as negative controls to avoid non-specific interaction. Besides, we provided evidence that Cep78, Ift20 and Ttc21a formed a complex, as they all co-fractioned in a testicular protein complex at the size between158 kDa to 670 kDa using size exclusion chromatography (Figure 7E). Additionally, we performed super-resolution analysis of immunofluorescent localizations, and observed co-localization between Cep78 and Ttc21a or Ift20 by SIM. With these data, we think that Cep78 interacts with Ttc21a and Ift20 and they form a complex. We rephrased “direct interaction” as “interaction” in the manuscript.

Reviewer #3 (Public Review):

Authors were aiming to bring a deeper understanding of CEP78 function in the development of cone-rod dystrophy as well as to demonstrate previously not reported phenotype of CEP78 role in male infertility.

It is important to note, that the authors 're-examined' already earlier published human mutation, 10 bp deletion in CEP78 gene (Qing Fu et al., 10.1136/jmedgenet-2016-104166). This should be seen as an advantage since re-visiting an older study has allowed noting the phenotypes that were not reported in the first place, namely impairment of photoreceptor and flagellar structure and function. Authors have generated a new knockout mouse model with deleted Cep78 gene and allowed to convey the in-depth studies of Cep78 function and unleash interacting partners.

The authors master classical histology techniques for tissue analysis, immunostaining, light, confocal microscopy. They also employed high-end technologies such as spectral domain optical coherence tomography system, electron, and scanning electron microscopy. They performed functional studies such as electroretinogram (ERG) to detect visual functions of Cep78-/- mice and quantitative mass spectrometry (MS) on elongating spermatids.

The authors used elegant co-immunoprecipitation techniques to demonstrate trimer complex formation.

Through the manuscript, images are clear and support the intended information and claims. Additionally, where possible, quantifications were provided. Sample number was sufficient and in most cases was n=6 (for mouse specimens).

The authors could provide more details in the materials and methods section on how some experiments were conducted. Here are a few examples. (i) Authors have performed quantitative mass spectrometry (MS) on elongating spermatids lysates, however, did not present specifically how elongating spermatids were extracted. (ii) In the case of co-IPs authors should provide information on what number of cells (6 well-plate, 10 cm dish etc) were transfected and used for co-IPs. Furthermore, authors could more clearly articulate what were the novel discoveries and what confirmed earlier findings.

The authors clearly demonstrate and present sufficient evidence to show CEP78/Cep78 importance for proper photoreceptor and flagellar function. Furthermore, they succeed in identifying trimer complex proteins which help to explain the mechanism of Cep78 function.

The given study provides a rather detailed characterization of human and mouse phenotype in response to the CEP78/Cep78 deletion and possible mechanism causing it. CEP78 was already earlier associated with Cone-rod dystrophy and, this study provides a greater in-depth understanding of the mechanism underlying it. Importantly, scientists have generated a new knock-out mouse model that can be used for further studies or putative treatment-testing.

CEP78/Cep78 deletion association with male infertility is not previously reported and brings additional value to this study. We know, from numerous studies, that-testes express multiple genes, some are unique to testes some are co-expressed in multiple tissues. However, very few genes are well studied and have clinical significance. Studies like this, combining patient and animal model research, allow to identify and assign function to poorly characterized or yet unstudied genes. This enables data to use in basic research, patient diagnostics and treatment choices.

We would like to thank Reviewer #3 (Public Review) for positive comments on our work.

As to the suggestions to provide some details in the materials and methods by the reviewer, we added the description of STA-PUT method for spermatids purification at Page 34, Line 729-741 in the revised manuscript, the amount of cells used for co-IPs “10 cm dish HEK293T were transfected (Vazyme, Nanjing, China) wit 5μg plasmid for each experimental group.” at Page 36, Line 783-784 in the revised manuscript.

We also highlighted our new discovery and ensured that all previous published findings are accompanied by references, we added “We further explored whether c.1629-2A>G mutation in this previously visited patient would disturb CEP78 protein expression and male fertility. Blood sample was collected from this patient and an unaffected control for protein extraction.” at Page 17, Line 335. We also added “The major findings of our study are as follows: we found CEP78 as the causal gene of CRD with male infertility and multiple morphological abnormalities of the sperm flagella using Cep78-/- mice. A male patient carrying CEP78 c.1629-2A>G mutation, whom we previously reported to have CRD [8], was found to have male infertility and MMAF in this study. Cep78 formed a trimer with sperm flagella formation enssential proteins IFT20 and TTC21A (Figure 8), which are essential for sperm flagella formation[16, 18]. Cep78 played an important role in the interaction and stability of the trimer proteins, which regulate flagella formation and centriole length in spermiogenesis. ” at the first paragraph of discussion, which is Page 21, Line 447-456 of our revised manuscript.

Author Response

Reviewer #1 (Public Review):

The idea that a passive living being can improve the wind dispersal of its seeds by passively changing their drag is enticing. The manuscript shows that high wind events in Scotland are inversely correlated with the ambient humidity. The dandelion pappus morphs with the ambient humidity, being more open in dry conditions, which is associated with stronger wind events. This passive morphing of the shape of the pappi thus leads to a dispersal of the seeds further away from their origin.

The analysis and discussion in the paper is focused on "distance", i.e., how far the pappus will fly. Could the notion of time be relevant too? In wet conditions, perhaps it's better for a seed to hit the ground quickly and start germinating, whereas if its dry, staying up in the air for longer to travel farther might be a better strategy.

This is an interesting point; however, we think that flight time is likely to be less relevant to the dispersal outcomes. This is because seeds mostly remain attached to the parent plant in wet conditions so will not fly at all and therefore will not begin germination. When they do disperse, flight time will generally be only a few seconds for the majority of seeds whether they are wet or dry, and the timescale of wet weather is generally much longer (typically hours).

Author Response

Reviewer #1 (Public Review):

This excellent manuscript challenged the premise that NF-kappaB and its upstream kinase IKKbeta play a role in muscle atrophy following tenotomy. Two animal models were used - one leading to enhanced muscle-specific NF-kappaB activation and the other a muscle-specific deletion. In both models, there was no significant relationship to observed muscle changes following tenotomy. Overall this work is significant in that it challenges the existing dogma that NF-kappaB plays a crucial role in muscle atrophy.

Surprisingly the authors noted that there were basal differences observed in the phenotypes of their models that were sex-dependent. They note that male mice lose more muscle mass after tenotomy and specifically type 2b fiber loss.

Overall this is an outstanding study that challenges the notion that NF-kappaB inhibitors are likely to improve muscle outcomes following injuries such as rotator cuff tears. Its main weakness is that there were no pharmacological arms of investigation; this fails to definitively exclude the hypothesis that inhibition may exert some effect in healing, perhaps in surrounding non-muscle matrix tissue that in turn may assist in healing.

Thank you for your careful and thoughtful review. We agree that the finding that NFkb is not driving tenotomy-induced atrophy is both surprising and interesting. We look forward to further uncovering the atrophic mechanisms responsible. We also agree that an investigation using pharmacological NFkb inhibitors will improve our understanding of the full scope of the role of NFkb in the tenotomy pathology. As you and another reviewer note, this work has only blocked NFkb signaling in the mature muscle fiber and thus cannot assess the role of NFkb in satellite cell, fibroblast, immune cell activation etc in the healing response. However, we avoided using these inhibitors in this study due to the potential for these systemic effects to obscure the role of NFkb in the muscle fiber. While we believe that a pharmacological investigation is beyond the scope of this study, it will make an excellent follow on investigation.

Reviewer #2 (Public Review):

The primary strength of this paper is a rigorous approach to 'negative' data. Did the authors definitively prove that NF-kB has no role in the tenotomy-induced atrophy? Probably not entirely, since there are limitations of the mouse model and the knockdown mice. There cannot be complete elimination of load since mice heal with some scar tissue, and the knockdown is not complete elimination. However, even with these limitations, this presents important findings that tenotomy, which induces mechanical unloading of the muscle-tendon unit, provides a unique biomechanical environment for the muscle to undergo atrophy, which warrants a more in-depth look given that these injuries are unique and extremely common. It must be mentioned that the results are entirely supported by their data and that even though the model is not 'perfect' it truly supports that NF-kB has a limited role in atrophy. The sex-mediated differences based on autophagy are a secondary hypothesis and are interesting but possibly less clinically relevant based on the differences shown.

We appreciate your thoughts on the “negative” data in this study. A manuscript in which the data refute your hypothesis and that of the field is difficult to write. There is a higher burden of validation and closer scrutiny of limitations. We agree that the model does have some limitations, but overall strongly supports a limited role for NBkb in tenotomy-induced muscle atrophy.

The important next step for this group and others is to evaluate the 'how and why' of tenotomy atrophy if not through NF-kB. Is it that there are many redundant processes that the muscle may have to circumnavigate the NF-kB pathway given that it is so ubiquitous that the authors didn't see a difference? Could it be differences in axial vs appendicular muscle? Or should there be a closer look at the mechanosensors in the muscle cells to determine if there are other key drivers of atrophy? Regardless, this paper shows that tenotomy-induced muscle atrophy is unique and supports the conclusion that muscle has many ways to atrophy based on the injury it undergoes.

We agree that the major next step for this work is to investigate the mechanism(s) responsible for tenotomy-induced atrophy. Autophagy in particular needs a more thorough investigation using autophagic inhibitors in naive wildtype mice to investigate its role in the sex-specificity of tenotomy-induced atrophy. The question of axial vs. appendicular muscle is intriguing. There could also be an upper vs. lower body difference that is worth exploring in future work.

Reviewer #3Public Review):

The authors provided thorough analyses of muscle morphology, biochemistry, and function, which is a major strength of the study. However, there are some key confounding variables authors failed to address. For example, the difference in the estrous cycle in female animals was not controlled. The study could have been significantly improved by controlling sex hormone levels or at least testing differences in response to injury.

We appreciate your careful and insightful review of our work. We designed this study to assess the role of myofiber NFkb in tenotomy-induced atrophy, which led us to a rigorous assessment of morphology, biochemistry and function, which we agree is the strength of the study. We also agree that a major limitation of this study is that the secondary observations of sex-specificity and autophagic signaling are not as well controlled or supported. This is because these observations were made at the end of the study when the histological analyses were completed by the blinded rater. The sex-specificity in the basophilic puncta that the rater observed sparked us to reconsider the sex-specificity in our other data and to stain for autophagic vesicles. As you suggest, to rigorously assess sex-specificity it would be good to control of estrous cycle and analysis of sex hormones which would require initiation of another study, planning for these variables in advance. We think this is beyond the scope of the current question of the role of NFkb in tenotomy-induced atrophy but think it should be undertaken as a follow on to eliminate confounding variables of genetic manipulation and tamoxifen treatment.

However, since we still need to report the sex specificity we observed while ensuring that our findings are not misconstrued, we reviewed the language in the manuscript to emphasize that these are retrospective observations that require further investigation. We have also added discussion of these variables and their potential influence on the results to the Discussion.

Discussion: “Additionally, it is important to note that estrous cycle was not controlled in these mice and sex hormone levels weren’t measured in this study. These preliminary observations, though intriguing, will require more rigorous follow up evaluations to define the interaction between sex, tenotomy, and autophagy in naïve wildtype mice.”

Furthermore, more data are needed to link NFkB signaling and autophagy to make any kind of conclusions. Overall, in the current form of the manuscript, the presented data seem underdeveloped, and the addition of more supporting data could significantly improve the quality of the manuscript and enhance our understanding of NFkB signaling and muscle wasting in rotator cuff injury.

We agree that more data are needed to complete the picture of autophagy in tenotomy-induced muscle atrophy. The p62 and LC3 positive intracellular puncta in male tenotomized muscle are distinctive, but only limited conclusions can be drawn physiologically because 1) they are only present in a fraction of fibers and 2) it is impossible to tell whether they result from increased autophagic flux or altered vesicle processing. Western blot for LC3 (and now p62) indicates only small changes in total protein, but since these proteins are synthesized and degraded during active autophagy, it is possible for their levels to remain constant while flux increases. Direct measures of autophagic flux would require treating mice with an autophagosome block which would require initiation of another study. However, we agree with the reviewer that we can add some additional measures to better characterize the instantaneous state.

We have added analysis of p62 protein expression to LC3 since p62 protein content in muscle can be decoupled from LC3 (PMID: 27493873). We also added expression data for genes involved in autophagy (Lc3b, Gabarapl1, Becn1, Bnip3, and Atg5). Finally, we have commented on the limitations of our data in the Discussion.

Discussion: “Evidence for autophagy regulating tenotomy-induced atrophy has been mounting over recent years (Bialek et al., 2011; Gumucio et al., 2012; Joshi et al., 2014; Ning et al., 2015; Hirunsai & Srikuea, 2021). The evidence presented here supports this contention, but we find surprisingly small effect sizes for all markers investigated. This could be because we are not directly assessing autophagic flux and so are missing some temporal dynamics since synthesis and degradation are ongoing simultaneously.”

Author Response

Reviewer #1 (Public Review):

The authors have generated a set of seven nanobody tools against two of the largest Drosophila proteins, which are related to vertebrate titin and essential for muscle function. The study of such gigantic proteins is a challenge. They show that each of these nanobodies recognizes their epitope with high affinity (as expected from antibodies), fails to generate a signal after immune-fixation of a mutant for the cognate protein, do not cross-react with each other, and generates a signal in the muscle that makes sense with what one would anticipate for fly titin homologs. In addition, they show that these nanobodies have better penetration and labeling efficiency than conventional antibodies in thick tissues after classical paraformaldehyde fixation. Using these nanobodies, they could deduce the organization of the epitopes in different muscle types and propose a model for Sallimus and Projectin arrangement in muscles, including in larvae which are difficult to label with traditional antibodies due to their impermeable chitin skeleton. Finally, they could fuse the gene encoding one of the nanobodies to the open reading frame of NeonGreen and express the corresponding fusion protein in animals to use the probe in FRAP assays.

The work is very well performed and convincing. However, given its significant redundancy in terms of biological conclusions with the companion study "Nanobodies combined with DNAPAINT super-resolution reveal a staggered titin nano-architecture in flight muscles" by the same authors, and other published papers, I recommend the authors further prove the use of their nanobodies in live assays. In particular, the authors should test whether they can use the nanobodies to induce protein degradation either permanently or conditionally.

Thanks for this nice summary of our findings. We have now extended the analysis of the Nanobody-NeonGreen fusion expressing larval muscles and provide first proof of principle analysis of new fly strains that we generated that contain Sls-Nano2 or Sls-Nano42 nanobodies fused to a degradation signal. These induce lethality of the animals suggesting that Sls protein is partially non functional. We verified this by providing quantitative stainings of various Sls epitopes in these muscles suggesting that Sls is not fully degraded but rather partially modified in the Sls-Nano-deGrad expressing muscle fibers. These will be interesting tools to study Sls function during sarcomere homeostasis.

Reviewer #2 (Public Review):

The data presented in this manuscript are sound but rather descriptive. The contribution - as presented - is mostly of a technical nature. The authors correctly state that anti-GFP nanobodies, while used extensively across many model organisms, have limited utility for in vivo applications when the GFP-tagged protein in question displays abnormal behavior or is non-functional. The creation of nanobodies that are uniquely specific for the protein(s) of interest is therefore a significant improvement, especially since the Sallimus and Projectinspecific reagents reported here react with PFA-fixed material. At least one of these nanobodies, when expressed in vivo, decorates the appropriate target. The source of antigens used for the construction of the nanobody library is Drosophila-derived. The extent of homology of Drosophila Sallimus and Projectin with related proteins in other species is not discussed. Whether the nanobodies reported here would be useful in other (closely related?) species, therefore, remains to be established. For those studying muscle biology in Drosophila, the nanobodies described here will be publicly available as cDNAs. Ease of production implies a readily shared and standardized resource for the field.

We thank this reviewer for appreciating that our Sallimus and Projectin nanobodies are useful. We now have extended the collection even further, including anti-Obscurin, αActinin and Zasp52 nanobodies, the latter two will also be useful for researcher studying other tissues, in particular Drosophila epithelial tissues. As always in the Drosophila field, all the here generated fly strains and plasmids will be made easily available to the community by placing them in stock centers or shipping them to the laboratories directly. As indicated, also the plasmids will be deposited at Addgene.

Further characterization of these nanobodies by biochemical methods such as immunoblotting would be challenging, given the size of the target proteins. In view of the technical nature of this manuscript, the authors should perhaps critically discuss the distinction between bulky GFP tags versus the much smaller epitope tags and the nanobodies that recognize them, although this was covered in a recent eLife paper from the Perrimon lab. Insertion of small tags, in conjunction with nanobodies that recognize them, would be less perturbing than the much bulkier GFP tag and lend itself to genome-wide applications. Creating nanobodies uniquely specific for each protein encoded in the Drosophila genome is not realistic, and the targeted approach deployed here is obviously valuable.

We are discussing the drawbacks of solely relying on GFP nanobodies, which requires GFP tagged proteins to be available and being functional. In particular for the sarcomeric proteins this is often not the case. We also cite the Perrimon paper, which was just published as we prepared this manuscript. We would like to point out to this reviewer that even tagging with a small epitope tag is considerable work in Drosophila and that the Perrimon paper, on which this reviewer is an author, does describe only two endogenously tagged genes with a nanotag (histone H2Av and Dilp2) the other genes described were expressed from a UAS source or in cell culture. We show here 22 nanobodies against 11 target epitopes.

Nanobodies recognise typically folded epitopes and are rather unlikely to work in immunoblotting.

The authors apply two different approaches to characterize the newly generated Nanobodies: more or less conventional immunohistochemistry with fluorescently labeled nanobodies, and in vivo expression of nanobodies fused to the fluorescent neongreen protein. The superiority of nanobodies in terms of tissue penetration has been shown by others in a direct comparison of intact fluorescently labeled immunoglobulins versus nanobodies. The authors state that in vivo labeling with nanobody fusions "thus far was done only with nanobodies against GFP, mCherry or short epitope tags." There is no fundamental difference between these recognition events and what the authors report for their Sallimus and Projectin-specific reagents. The section that starts at line 304 is thus a little bit of a 'straw man'. There is no reason to assume that a nanobody that recognizes a muscle protein would behave differently than a nanobody that would recognize that same protein (or another) when epitope- or GFP-tagged. What might be interesting is to examine the behavior of these muscle-specific nanobodies in the course of muscle contraction/relaxation: are there conformational alterations that promote dissociation of bound nanobodies? Do different nanobodies display discrete behavior in this regard? The manuscript is silent on how muscles behave in live L3 larvae. The FRAP experiment seems to suggest that not much is happening, but the text refers to the contraction of larval sarcomeres from 8.5 µM to 4.5 µM. Does the in vivo expressed nanobody remain stably bound during this contraction/relaxation cycle? What about the other nanobodies reported in this manuscript? Since the larval motion was reduced by exposure to diethylether, have the authors considered imaging the contractive cycle in the absence of such exposure?

We appreciate the expert knowledge about nanobodies by this reviewer. However, nanobodies were not extensively applied in Drosophila tissues. Hence, we believe it is important to characterise their penetration in stainings and compare them carefully to antibodies. Such, the Drosophila reader will be aware of their advantages.

We have now also included more data on the larval muscle morphology in the nanobody expressing muscles. Their morphology is normal. As larvae move around extensively all the time, the binding of the nanobodies to the target must be stable, otherwise it would not be bound when we fix them or anesthetize them. However, we have not attempted to image them at high resolution while crawling freely. From quantifying the crawling speed (about 1.5 mm per second, see Figure 9 S1) we hope this reviewer appreciates that high resolution imaging of sarcomeres in freely crawling larvae is highly non trivial.

Given that the nanobodies bind well-folded epitopes with low picomolar dissociations constants, it is hard to imagine that conformational changes of the target would dissociate them. The nanobody would stabilise the recognised conformation by a ΔG of ≈60 KJ/ mole, and we would not expect that the chosen domains undergo major conformational changes.

Reviewer #3 (Public Review):

Loreau et al. have presented a well-written manuscript reporting clever, original work taking advantage of fairly new biotechnology - the generation and use of single chain antibodies called nanobodies. The authors demonstrate the production of multiple nanobodies to two titin homologs in Drosophila and use these nanobodies to localize these proteins in several fly muscle types and discover interesting aspects of the localization and span of these elongated proteins in the muscle sarcomere. They also demonstrate that one of these single chain antibodies can be expressed in muscle fused to a fluorescent protein to image the localization of a segment of one of these giant proteins called Sallimus in muscle in a live fly. Their project is well-justified given the limitations of the usual approaches for localizing and studying the dynamics of proteins in the muscle of model organisms such as the possibility that GFP tagging of a protein will interfere with its localization or function, and poor penetration of large IgG or IgM antibodies into densly packed structures like the sarcomere after fixation as compared to smaller nanbodies.

They achieved their goals consistent with the known/expected properties of nanobodies: (1) They demonstrate that at least one of their nanobodies binds with very high affinity. (2) They bind with high specificity. (3) The nanobodies show much better penetration of fixed stage 17 embryos than do conventional antibodies.

They use their nanobodies mostly generated to the N- and C-terminal ends of Sallimus and Projectin to learn new information about how these elongated proteins span and are oriented in the sarcomere. For example, in examining larval muscles which have long sarcomeres (8.5 microns), using nanobodies to domains located near the N- and C-termini, they show definitively that the predicted 2.1 MDa protein Sallimus spans the entire I-band and extends a bit into the A-band with its N-terminus embedded in the Z-disk and C-terminus in the outer edge of the A-band. Using a similar approach they also show that the 800 kDa Projectin decorates the entire myosin thick filament except for the H-zone and M-line in a polar orientation. Their final experiment is most exciting! They were able to express in fly larval muscles a nanobody directed to near the N-terminus of Sallimus fused to NeonGreen and show that it localizes to Z-disks in living larvae, and by FRAP experiments demonstrate that the binding of this nanobody to Sallimus in vivo is very stable. This opens the door to using a similar approach to study the assembly, dynamics, and even conformational changes of a protein in a complex in a live animal in real time.

We thank this reviewer for appreciating the quality and impact of our approach and the our obtained results.

There are only a few minor weaknesses about their conclusions: (1) They should note that in fact their estimate of the span of Sallimus could be an underestimate since their Nano2 nanobody is directed to Ig13/14 so if all of these 12 Ig domains N-terminal of their epitope were unwound it would add 12 X 30 nm = 360 nm of length, and even if unwound would add about 50 nm of length.

We are discussing the length contribution of the 12 Ig domains now more extensively in the DNA PAINT super-resolution paper, however not in this resource paper as the 50 nm difference was not resolved with the confocal microscopy applied here to the larval muscle sarcomere.

(2) They discuss how Sallimus and Projectin are the two Drosophila homologs of mammalian titin, however, they ignore the fact that there is more similarity between Sallimus and Projectin to muscle proteins in invertebrates. For example, in C. elegans, TTN-1 is the counterpart of Sallimus, and twitchin is the counterpart of Projectin, both in size and domain organization. The authors present definitive data to support Figure 9, their nice model for a fly larval sarcomere but fail to point out that this model likely pertains to C. elegans and other invertebrates. In Forbes et al. (2010) it was shown that TTN-1, which can be detected by western blot as ~2 MDa protein and using two polyclonal antibodies spans the entire Iband and extends into the outer edge of the A-band, very similar to what the authors here have shown, more elegantly for Sallimus. In addition, several studies have shown that twitchin (Projectin) does not extend into the M-line; the M-line is exclusively occupied by UNC-89, the homolog of Obscurin.

We thank this reviewer for pointing out the important C. elegans literature that we have now included in this revised manuscript. We apologise for initially omitting them. They are indeed highly relevant.

Reviewer #4 (Public Review):

Authors report the generation and characterisation of several nanobodies for giant Drosophila sarcomeric proteins, Sallimus and Projectin the functional orthologs of titin. They describe an efficient pipeline that could potentially help in designing and producing nanobodies for other proteins. There are several advantages to using nanobodies in comparison to conventional antibodies and the authors nicely demonstrate that the generated nanobodies allow to precisely map subcellular localisation and even the protein orientation in the case of Projectin. They also show that small nanobody molecules have superior penetration and labelling efficiencies with respect to classical antibodies. Finally, the authors select one of the nanobodies to test whether it will efficiently detect native proteins in living tissue. They confirm that Sls-Nano2NeoGreen binds Sls in vivo in muscles of temporarily immobilized 3rd instar larva allowing to reveal sarcomeric Sls pattern and to demonstrate by FRAP experiments that Sls does not exchange during a short time period.

This work is of significant value to a large audience. It provides a clear and precise pipeline for the generation of efficient nanobodies, which are invaluable tools of modern biology.

We thank this reviewer for expressing strong support for our manuscript and appreciating its value for a large readership.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Chou-Zheng and Hatoum-Aslan follow up on their previous studies that have characterized the collaborations between the type III-A CRISPR-Cas10 Csm complex and various cellular housekeeping nucleases. The authors have previously demonstrated that the Csm complex associates with several nucleases that are implicated in RNA degradation via pulldown and mass spectrometry analysis. They also previously showed that some of these enzymes, including PNPase, are important for CRISPR RNA (crRNA) maturation and for robust anti-phage defense. They now show that a second housekeeping enzyme, RNase R, is required for crRNA maturation. PNPase and RNase R act in concert to produce the mature crRNA. The authors also analyze the interactions between Csm5 and both housekeeping proteins. Finally, they demonstrate that PNPase and RNase R are important for robust anti-plasmid activity when using crRNAs that are complementary to low-abundance transcripts.

This is a well-written paper with clear figures and well-described experiments and results. The experiments in Figures 1 and 2 demonstrating the importance of RNase R for crRNA maturation are excellent. The biochemistry experiments in Figure 2 are especially convincing, in which the authors were able to reconstitute the concerted activities of RNase R and PNPase for crRNA biogenesis. The experiments in Figure 5 implicating PNPase and RNase R in robust anti-plasmid activity when targeting low-abundance transcripts are also clear and convincing, and the result is intriguing. Overall, these experiments provide a new example in a growing list of co-opted host proteins that are important for crRNA biogenesis and CRISPR-mediated defense.

Thank you for your thoughtful review of our manuscript and comments overall!

I do have some concerns about experiments in Figures 3 and 4 analyzing interactions between PNPase or RNase R and the Csm5 subunit of the Csm complex, and I believe that some of the authors' conclusions are not fully supported by the evidence presented in these experiments. These concerns, along with a question about their model, are detailed below.

1) The authors used the structure of S. thermophilus Csm5 to guide their design of truncations to probe potential intrinsically disordered regions (IDR1 and IDR2) that may be sites of interaction with PNPase or RNase R. Since the authors submitted their manuscript, an AlphaFold predicted structure of the S. epidermidis Csm5 has been released on the AlphaFold Protein Structure Database. In this model, the IDR2 region is predicted by AlphaFold to be a beta strand at the center of a beta sheet, rather than a disordered region. If the prediction is accurate, deletion of this strand could cause Csm5 to misfold, making it difficult to interpret what causes loss of interaction with PNPase (i.e. deletion of a specific interaction surface versus misfolding of the overall tertiary structure). In light of this, the discussion surrounding these experiments should be altered to include more caveats about the truncations, and conclusions based on this experiment should be softened.

While this manuscript was under review, several cryo-EM structures of the Cas10-Csm complex from S. epidermidis were solved and reported (Smith et al, 2022, Structure). In the unbound complex (PDB ID 7V02), IDR2 of Csm5 does indeed overlap with a short beta strand, but it is flanked by loops/unstructured regions. In addition, of the 46 residues that we deleted in the Csm546 mutant, 20 residues are unresolved in the experimentally-determined structure, supporting the notion that this region is generally flexible. Also, it is unlikely that this and the other Csm5 deletion mutants are misfolded because they all retain the ability to associate with the complex (Fig. 4B), and we were able to readily purify the mutant with the largest deletion (Csm546) without any issues (Fig. 5). To address this concern, we added panel D in Figure 4-figure supplement 1, which highlights the IDR regions in Csm5 from the recently-published S. epidermidis Cas10-Csm complex structure and integrated the observations mentioned above in the narrative (lines 241-247 in the marked-up revised manuscript). We also softened the conclusions based on these experiments (lines 276-278 in the marked-up revised manuscript): “Taken together, these results suggest that the IDR2 region of Csm5 likely plays a role in the recruitment and stimulation of PNPase, while the binding site for RNase R may reside elsewhere in Csm5”.

2) The native gels testing interactions between Csm5 and RNase R show a slight change in mobility of RNase R upon the addition of Csm5. Although I agree with the authors' interpretation that this shift could be due to transient interactions between Csm5 and RNase R, it is also possible that the mobility of RNase R is affected simply based on the addition of a large excess of a second protein, even without a specific interaction between the two proteins. As a result, the evidence for direct interaction with Csm5 is limited. Discussion of how RNaseR is recruited by the Csm complex could contain more possible explanations. For example, it is possible that the interaction between RNase R and the Csm complex is mediated by another protein (e.g. PNPase could bridge interaction between the two) or that such an interaction could be stabilized by intermediate crRNA or target RNA binding by the Csm complex.

Thank you for this comment. To help rule out the possibility that excess Csm5 could cause a shift of any protein nonspecifically, we included a control in the original manuscript in which the same native gel assay was performed with BSA and Csm5, and found that Csm5 fails to cause an upward shift in BSA (Figure 3-figure supplement 1). In addition, to bolster the claim of a direct interaction between Csm5 and RNase R, we performed an additional pulldown assay (Figure 3-figure supplement 2). Details are described under the essential revisions point number 3 above. Regarding the other possibilities mentioned, it is unlikely that PNPase is bridging the interaction with RNase R because when we delete PNPase from cells, we still get some maturation (Fig. 1E and Chou-Zheng and Hatoum-Aslan, eLife, 2019). Also, in the reconstituted system, RNase R can still perform some level of maturation on its own (Fig. 2D). These observations argue against the need for bridging interactions with PNPase. Furthermore, maturation occurs in the absence of target RNA, ruling out the possibility that target RNA bridging is necessary for RNase R-mediated crRNA maturation. However, we agree with the reviewer that it is possible that other components of the Cas10-Csm complex may help to recruit and stabilize the interaction with RNase R in vivo, and this possibility was already mentioned in the narrative in the original submission, although we did not explicitally state the intermediate crRNA as one such component (lines 213-215 and again in lines 413-416 in the marked-up revised manuscript). We have replaced “subunits” with “components” in line 415 to be more inclusive of this possibility. Since this is all still speculative, we opt not to elaborate further on this point in the current manuscript. Needless to say, we are actively pursuing other more quantitative assays to measure the interactions between Csm5 and PNPase/RNase R and hope to have such data available in a follow-up manuscript.

3) On lines 367-391, the authors propose a model for how PNPase and RNase R may contribute to defense against foreign DNA through their recruitment by the Csm complex to the target transcript. However, their experiments do not test whether PNPase and RNase R must interact with the Csm complex to support anti-plasmid activity. Indeed, it may make more sense for free RNase R to be involved in defense, similar to how free activated Csm6 degrades transcripts non-specifically, rather than only cleaving transcripts in close proximity to the Csm complex. The authors could expand their discussion to mention the possibility that free RNase R or PNPase are acting in anti-plasmid defense.

Thank you for this suggestion. The following statement has been added to the discussion (lines 393-395 in the marked-up revised manuscript): “Once recruited by the complex, PNPase and RNase R may degrade nucleic acids in the vicinity nonspecifically, similarly to Csm6.”

Reviewer #2 (Public Review):

This work follows up on an earlier publication that showed PNPase and RNase J2 play important roles in CRISPR RNA processing (doi: 10.7554/eLife.45393). Here, the authors show that RNase R also plays a critical role in CRISPR RNA maturation. In addition, they show that RNase R and PNPase are both recruited to the type III CRISPR complex (Cas10-Csm) via direct interactions with the Cmr5 subunit and that deletion of an intrinsically disordered region (IDR2) on Cmr5 selectively inhibits PNPase recruitment but not RNase R. The authors show unquantified stimulation of PNPase nuclease activity by Cmr5. Phage challenge assays are performed to test the impact of PNPase and RNase R deletion mutations on CRISPR-Cas mediated phage defense. Contrary to expectation, over-expression of the CRISPR system in cells that contain a deletion of PNPase and/or RNase R, maintain robust anti-phage immunity. The interpretation of this experiment is that RNase R and PNPase may be dispensable in an over-expression system that produces high (non-natural) concentrations of the Csm complex. They test this idea using a system that expresses the CRISPR-Cas components off of a chromosomally encoded locus (strain RP62a) and challenge these cells using a plasmid conjugation assay. In this iteration, deletion of PNPase has no impact on CRISPR performance, while deletion of RNase R "exhibited a moderate" attenuation of the immune response. In contrast, to either single gene deletion, the PNPase and RNase R double mutant showed a near complete loss of immunity.

Overall, the paper provides convincing evidence that PNPase and RNase R are involved in crRNA processing, and that they are recruited to the type III complex via Cmr5. The work on RNase R is entirely new and the role of PNPase is expanded. The role of cellular RNases in CRISPR RNA biogenesis is important, though some of the results are subtle and some of the biochemistry would benefit from a more quantitative analysis.

Thank you for your thorough assessment and comments overall.

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)

Author Response

Reviewer #1 (Public Review):

Current generative models of protein sequences such as Potts models, Variational autoencoders, or autoregressive models must be trained on MSA data from scratch. Therefore, they cannot learn common substitution or coevolution patterns shared between families, and require a substantial number of sequences, making them less suitable for small protein families (e.g., conserved only for eukaryotes or viruses). MSA transformers are promising alternatives as they can generalize across protein families, but there is no established method to generate samples from them. Here, Sgarbossa et al. propose a simple recursive sampling procedure based on iterative masking to generate novel sequences from an input MSA. The sampling method has three hyperparameters (masking frequency, sampling temperature, and the number of iterations) which are set by rigorous benchmarking. The authors compare their approach to bmDCA, and evaluate i) single sample quality metrics ii) sample diversity and similarity to native sequences iii) similarity between original and generated sequence distribution, and iv) phylogeny/topology in sequence space of the generated distribution.

Strengths:

• The proposed sampling approach is simple.

• The computational benchmarking is thorough.

• The code is well organized and looks easy to use.

Weaknesses:

• There is no experimental data to back up the methodology.

• It is not clear whether the sampling hyperparameter used is optimal for all protein sizes.

• I am unsure that the bmDCA baseline method was trained appropriately and that the sampling method was adequate for protein design purposes (regular sampling).

• Quality assessment of predicted structures is incomplete.

• The proposed metrics for evaluating the diversity of generated sequences are fairly technical.

We respond to each of these points below, in the section titled "Recommendations for the authors", since these questions were asked by the reviewer in more detail there.

Impact assessment: The claim that MSA Transformer could be useful for protein design is supported by the computational benchmark. This work will be useful for researchers interested in applying MSA-Transformer models for protein design

We thank the reviewer for this encouraging assessment of our work, and for their very interesting suggestions which helped us improve our manuscript.

Reviewer #2 (Public Review):

The manuscript by Sgarbossa et al. proposes the use of a machine learning technique used in Language Models (LM) and adapted to protein sequences (PLM) as a means to generate synthetic sequences that retain functional properties contained in the original multiple sequence alignment (MSA) of natural sequences. This technique (or a similar one) called MSA Transformers is also a component of the supervised learning methodology Alphafold which has been successful in predicting protein structures and complexes of proteins. The premise of this study is that an iterative masking approach can be used as a sampling technique to create a diverse set of sequences that still preserve important properties of the original natural sequences. For example, such samples retain homology properties, score well in terms of retaining relevant pairwise or epistatic interactions, and produce "foldable" sequences when used as input for Alphafold and scored via its confidence metric pLDDT. In order to provide support for this claim, the authors compare against Direct Coupling Analysis (DCA), which is a global sequence modeling technique that has shown to be successful in many aspects of the structure and function of proteins and particularly in generating and sampling sequences analogous to the input MSA. Most importantly, DCA and its generative version bmDCA have been shown to produce functional sequences experimentally. The authors then establish that the properties of sequences of the MSA Transformer with iterative masking, have in general better scores in terms of homology, statistical energies, and pLDDT scores than the ones from bmDCA and have spectral, statistical and similarity properties more akin to the natural sequences than those from the bmDCA methodology, except for the reproduction of single and pairwise statistics. The sequences from the MSA Transformer, however, replicate better the three body statistics of the natural sequences. The authors conclude that MSA Transformers with iterative masking is a valid technique for sequence design and it is an important alternative to the use of DCA or de novo physics-based methods or supervised learning techniques.

Given the success of the use of language models in machine learning and its contributions to the structure prediction of protein and complexes, I see this study as a required follow-up to the breadth of work of amino acid coevolution spearheaded by DCA methodologies. In general, I believe this is a useful and relevant study for the community and opens up several avenues for research connecting Transformers with unsupervised protein design. Although the study provides support for this technique to be potentially useful for protein design, I was not completely convinced that it will yield more transformative results than the ones using Potts models. The differences, although consistent across the study, seem to be within "the margin of error" compared to bmDCA.

We thank the reviewer for this positive assessment of our work, and for their cogent remarks which helped us improve our manuscript.

We agree that in the case of large protein families, the main message is that our sequence generation method based on MSA Transformer scores at least as well as bmDCA. Given that bmDCA has been experimentally validated as a generative model, we believe that this is a valuable result. Our revised manuscript makes this point stronger, by showing that our sequence generation method based on MSA Transformer yields sequences that score similarly to those generated by bmDCA at low sampling temperature, while retaining substantially more sequence diversity.

In addition, following the reviewer's suggestion below, we now present results for smaller protein families, whose shallow MSAs make it difficult to accurately fit Potts models. These results are presented in a new section of Results, titled "Sequence generation by the iterative masking procedure is successful for small protein families", including the new Figure 3. As mentioned there, "Fig. 3 reports all four scores discussed above in the case of these 7 small families, listed in Table S1 (recall that the families considered so far were large, see Table 1). We observe that MSA-Transformer–generated sequences have similar HMMER scores and structural scores to natural sequences. MSA-Transformer–generated sequences also generally have better HMMER scores and structural scores than those generated by bmDCA with default parameters. While low-temperature bmDCA yields better statistical energy scores (as expected), and also gives HMMER scores and structural scores comparable to natural sequences, it in fact generates sequences that are almost exact copies of natural ones (see Fig. 3, bottom row). By contrast, MSA Transformer produces sequences that are quite different from natural ones, and have very good scores." This shows that our method not only performs as well as bmDCA for large families, but also has a broader scope, as it is less limited by MSA depth than bmDCA.

I also have certain comments related to the use of these 3 metrics to analyze the performance of the sampling. On the one hand, HMMER which has had a great utility for Pfam and the community in general is a score that is not necessarily reflecting the global properties of the sequences. In other words, we might be using a simpler statistical model to evaluate the performance of two other models (MSA Transformers and bmDCA) which are richer and that capture more sequence dependencies than the hidden Markov model.

We agree with the reviewer that HMMER scores are associated with simpler statistical models, which cannot fully represent the data. We nevertheless believe that these scores remain useful to assess homology. In the framework of our study, they show that the sequences we generate are deemed "good homologs" by HMMER - similarly to natural sequences that would be extracted from a database by this widely-used tool. This said, we agree with the reviewer that one should not overinterpret HMMER scores, and we have reduced our discussion of their correlations with Hamming distances to avoid giving too much importance to this point.

Moreover, we now present new scores that give a more complete picture of the quality of our generated sequences:

• Regarding structure, in addition to the AlphaFold pLDDT score, we now also report the RMSD between a reference experimental structure of the relevant family (see Table 1) and the AlphaFold structure predicted for each sequence studied. The results from the RMSD analysis corroborate those obtained with pLDDT and show that predicted structures are indeed similar to the native ones. These results are now discussed in the main text. We believe that this point strengthens our conclusions and we thank the reviewer for suggesting this analysis.

• We also performed a retrospective validation using published experimental results. For chorismate mutase, a protein family which was experimentally studied in [Russ et al 2020] using bmDCA, we now report estimated relative enrichments for our generated sequences in Figure S8, in addition to our four usual scores now shown for this family in Figure S7. In addition, for protein families PF00595 and PF13354, we now report deep mutational scanning scores for our generated sequences in Figure S9. These results strengthen our conclusion that our sequence generation method based on MSA Transformer is highly promising.

For the case of the statistical energy score, the authors decided to use a sampling temperature T=1, but the authors note that this temperature can be reduced, as it was done in the experimental paper, to produce sequences with better energies, therefore this metric can be easily improved by modifying the temperature. The authors mentioned that they did try to reduce the temperature and that they also improved their HMMER score, however, they decided against it because the pairwise statistics were affected. However, pairwise statistics was precisely the only factor where bmDCA seemed superior to the MSA transformer, so reducing it should be an acceptable trade-off in order to optimize the other two important metrics.

We thank both reviewers for raising this very interesting point. As mentioned above in our response to the first reviewer, we have now performed a comprehensive comparison of our MSA Transformer-generated data not only to bmDCA-generated data at sampling temperature T=1 but also at lower sampling temperatures. We considered the two temperature values chosen in [Russ et al 2020], namely T=0.33 and T=0.66. For completeness, we also considered the two values of regularization strength λ from [Russ et al 2020] for these three temperatures, in the case of family PF00072, as reported in Table S5. Given the relatively small impact of λ observed there, we kept only one value of λ for each value of T in the rest of our manuscript namely, λ=0.01 for T=1 to match the parameters in [Figliuzzi et al 2018], and λ=0.001 for T=0.33 and T=0.66 as it gave slightly better scores in Table S5. Note that for our additional study of small protein families, we employed λ=0.01 throughout because it is better suited to small families. In particular, we now include results obtained for bmDCA at λ=0.001 and T=0.33 in all figures of the revised manuscript.

Our general findings, which are discussed in the revised manuscript, are that decreasing T indeed improves the scores of bmDCA-generated sequences. However, the main improvement regards statistical energy (as expected from lowering T), while the improvements of other scores (HMMER score, and, more importantly, structural scores) are more modest. Even using T=0.33 for bmDCA, our MSA Transformer-generated sequences have similar or better scores compared to bmDCA-generated sequences, apart from statistical energy (see Figure 1 and Tables S2 and S3). Moreover, we find that decreasing T with bmDCA substantially decreases MSA diversity, while MSA Transformer-generated sequences do not suffer from such an issue (see Figure S1). In fact, at low T, bmDCA concentrates on local minima of the statistical energy landscape (see Figures 2, 5 and S5), resulting in low diversity.

Overall, these new results confirm that our procedure for generating sequences using MSA Transformer is promising, featuring scores comparable with low-temperature bmDCA sequences and high diversity.

Finally, the use of pLDDT could also present some biases, since Alphafold itself uses transformers, I wonder if this fact could lead to the fact that sequences obtained with transformers simply perform better by definition.

We thank the reviewer for raising this intriguing point. It is true that MSA Transformer has an architecture that is very similar to that of the EvoFormer module of AlphaFold. However, AlphaFold couples the EvoFormer module to a structural module, and is trained in a supervised way to predict protein structure, which makes it significantly different from MSA Transformer.

Nevertheless, we agree that the AlphaFold pLDDT score does not give a complete view of structure. As mentioned above, to improve this, in addition to pLDDT, we now also report the RMSD between a reference experimental structure of the relevant family (see Table 1) and the AlphaFold structure predicted for each sequence studied. The results from the RMSD analysis corroborate those obtained with pLDDT and show that predicted structures are indeed similar to the native ones. These results are now discussed in the main text.

The authors should try to address all these concerns. My assessment is that these concerns do not demerit the relevance and how timely this study is, but I would like to see a more fair comparison of these metrics where more optimizations to bmDCA are made, e.g. lower T, to have a more accurate comparison of the methods, even if that is reflected in lower performance on pairwise statistics.

We did our best to address all these points. We believe that the additions mentioned above have substantially improved our manuscript.

My assessment is that this manuscript's main strength is in introducing a state-of-the-art technique that has already been extremely successful in the field of computer science and artificial intelligence into the field of amino acid coevolution. By adapting this technique and creating a sampling version that is compatible with other successful methodologies, this work will lead to many other studies dealing with function and the effects of sequence variation of biomolecules.

Again, we thank the reviewer for their encouraging assessment.

Author Response

Reviewer #1 (Public Review):

This fMRI study investigated how memories are updated after reinterpreting past events. Participants watched a movie and subsequently recalled individual scenes from that movie. Importantly, the movie ends with a twist that changes the interpretation of earlier scenes in the movie. One group of participants watched the movie with the twist at the end, one group did not get to see the twist, and a third group was already informed about this twist before watching the movie. Analyses compared the similarity of activity patterns to (encoded or recalled) events across participants within regions of the default mode network (DMN). The design allowed for multiple relevant comparisons, confirming the prediction that activity patterns in DMN regions reflect the (re)interpretation of the movie (during movie viewing and/or during recall).

The study is well-designed and executed. The inclusion of multiple analyses involving distinct comparisons strengthens the evidence for the role of the DMN in memory updating.

The following points may be relevant to consider:

1) The cross-participant pattern analysis method used here is not standard, with such analyses typically done within participants (or across participants, but after aligning representational spaces). Considering individual variability in functional organization, the method is likely only sensitive to coarse-scale patterns (e.g., anterior vs posterior parts of an ROI). This is not necessarily a weakness but is relevant when interpreting the results.

We agree with the reviewer that functional misalignment might have played against us here. We designed this study as a natural successor of our previous work in which we captured reliable and multimodal scene-specific cross-participant pattern similarity during encoding and recall in standard space. In this revised version, we provide further evidence on how scene content is captured and influences our results. Nonetheless, we agree with your comment and add the following section to the discussion to encourage considering this point while interpreting the results.

"Moreover, our current method relies on averaging spatially-coarse activity patterns across subjects (and time points within an event). Future extensions of this work may benefit from using functional alignment methods (Haxby et al 2020, Chen et al 2015) to capture more fine-grained event representations which are shared across participants."

2) Unlike previous work, analyses are not testing for scene-specific information. Rather, each scene is treated separately to establish between-group differences, and results are averaged across scenes. This raises the question of whether the patterns reflect scene-specific information or generic group differences. For example, knowing the twist may increase overall engagement, both when viewing the movie (spoiled group) and when recalling it (spoiled group + twist group). The DMN may be particularly sensitive to such differences in overall engagement.

You have brought up great points. We addressed them in two ways: (1) We ran a univariate analysis in each DMN ROI to look at the role of overall regional-average response magnitude in our results. We did not observe a significant effect of group or an interaction between group and condition. (2) We ran a scene-specificity analysis in a new Results section entitled “The role of scene content” (Figure 4). This section is focused on comparing interaction index (Figure 2C), as an indicator of memory updating, under different manipulations. Interaction index reflects the reversal of neural similarity during encoding and recall. Our results suggest that we don’t see the same effects if we shuffle the scene labels and recompute the pattern similarity analyses. Please see added text and figures below:

"To test whether our reported results were mainly driven by the similarities and differences in multivariate spatial patterns of neural representations, as opposed to by univariate regional-average response magnitudes, we ran a univariate analysis in each ROI. This analysis revealed no significant effect of group (“spoiled”, “twist”, “no-twist”) or interaction between group and condition (movie, recall) (Table 1, see Methods for details).

Next, to determine whether scene-specific neural event representations—as opposed to coarser differences in general mental state across all scenes with similar interpretations—drive our observed pISC differences, we shuffled the labels of critical scenes within each group before calculating and comparing pISC across groups. By repeating this procedure 1000 times and recalculating the interaction index at each iteration, we constructed a null distribution of interaction indices for shuffled critical scenes (light magenta distributions in Figure 4B). In 12 out of 24 DMN regions, interaction indices were statistically significant based on the shuffled-scene distribution (p < .025, FDR controlled at q < .05). All of these 12 regions were among the ROIs that showed meaningful effects in our original analysis (Figure 2C). Regions with significant scene-specific interaction effects are marked as blue dots with black borders in Figure 4B. Overall, the findings from this analysis confirm that our results are driven by changes to scene-specific representations."

3) The study does not reveal what the DMN represents about the movie, such that its activity changes after knowing the twist. The Discussion briefly mentions that it may reflect the state of the observer, related to the belief about the identity of the doctor. This suggests a link to the theory of mind/mentalizing, but this is not made explicit. Alternatively, the DMN may be involved in the conflict (or switching) between the two interpretations.

Great points. We added to the discussion about the role of mentalizing network and in the particular temporo-parietal cortex. About your last point, we think our whole brain findings outside DMN (ACC and dlPFC) might relate to that point. We discussed these further in the paper.

"We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

In our whole brain analysis, these regions did not have significant interaction effects, which suggests that the effects were isolated to encoding. In the whole-brain analysis, we also observed a significant encoding-encoding and interaction effects in anterior cingulate cortex, as well as recall-recall and interaction effects in dlPFC. These results suggest that both the "spoiled" manipulation and the "twist" may recruit top-down control and conflict monitoring processes during naturalistic viewing and recall."

4) The design has many naturalistic aspects, but it is also different from real life in that the critical twist involves a ghost. Furthermore, all results are based on one movie with a specific plot twist. It is thus not clear whether similar results would be obtained with other and more naturalistic plot twists.

We added this as a limitation of the study.

"Our findings provide further insight into the functional role of the DMN. However, these results have been obtained using only one movie. While naturalistic paradigms better capture the complexity of real life and provide greater ecological generalizability than highly-controlled experimental stimuli and tasks (Nastase et al., 2020), they are still limited by the properties of the particular naturalistic stimulus used. For example, this movie—including the twist itself—hinges on suspension of disbelief about the existence of ghosts. Future work is needed to extend our findings about updating event memories to a broader class of naturalistic stimuli: for example, movies with different kinds of (non-supernatural) plot twists, spoken stories with twist endings, or using autobiographical real-life situations where new information (e.g. discovering a longtime friend has lied about something important) triggers re-evaluation of the past (e.g. reinterpreting their friend’s previous actions)."

5) Only 7 scenes (out of 18) were included in the analysis. It is not clear if/how the results depend on the selection of these 7 scenes.

Thank you for bringing this up. These scenes were pre-selected for the analyses, as they are the only scenes that are rated high by our independent raters (not study participants) on “twist influence”, meaning that knowing the twist could dramatically change their interpretation. So, we had a priori reasons to hypothesize that the effect will be strong in these scenes. To address your point, we report results by including all 18 scenes in a new Results section entitled “The role of scene content” and in Figure 4A. While the effect was weaker for all scenes it was still apparent in this conservative analysis. As expected, however, including 7 critical scenes produces stronger results than including all scenes or the uncritical scenes (all minus critical scenes). Please see the “The role of scene content” in Results and in Figure 4 for more detailed information.

"The role of scene content In the prior analyses, we focused on “critical scenes”, selected based on ratings from four raters who quantified the influence of the twist on the interpretation of each scene (see Methods). An independent post-experiment analysis of the verbal recall behavior of the fMRI participants yielded “twist scores” that were also highest for these scenes; that is, the expected and perceived effect of twist information on recall behavior were found to match. In our next analysis, we asked whether the neural event representations reflect these differences in the twist-related content of the scenes. In other words, are the “critical scenes” with highly twist-dependent interpretations truly critical for our observed effects?

To answer this question, we re-ran our main encoding-encoding and recall-recall pISC analysis in each DMN ROI (Figure 2-3). We calculated interaction indices (Figure 2C) first by including all scenes, and second by including only the 11 non-critical scenes. To better compare the effect of including different subsets of scenes to our original results, in Figure 4 we show the results in 15 ROIs that exhibited meaningful effects in our main analyses (Figure 2C). Figure 4A demonstrates that “critical scenes” yielded higher interaction indices compared to all scenes or non-critical scenes across all ROIs. The interaction score across all DMN ROIs was significantly higher in “critical scenes” than all scenes (t(23) = 7.19, p = 2.53 x 10-7) and non-critical scenes (t(23) = 7.3, p = 1.95 x 10-7). These results show that critical scenes are indeed responsible for the observed pISC differences across groups."

Reviewer #2 (Public Review):

In this manuscript titled "Here's the twist: How the brain updates the representations of naturalistic events as our understanding of the past changes", the authors reported a study that examined how new information (manipulated as a twist at the end of a movie) changes the neural representations in the default mode network (DMN) during the recall of prior knowledge. Three groups of participants were compared - one group experienced the twist at the end, one group never experienced the twist, and one group received a spoiler at the beginning. At retrieval, participants received snippets of 18 scenes of the movie as cues and were asked to freely describe the events of each scene and to provide the most accurate interpretation of the scene, given the information they gathered throughout watching.

All three groups were highly accurate in the recall of content. The groups that experienced the twist at the end as well as at the beginning as a spoiler showed a higher twist score (the extent to which twist information was incorporated into the recall), while seemingly also keeping the interpretation without the twist ("Doctor representation") intact. Neurally, several regions in the DMN showed significant interaction effects in their neural similarity patterns (based on intersubject pattern correlation), indicating a change in interpretation between encoding and recall in the twist group uniquely, presumably reflecting memory updating.

Several points that I think should be addressed to strengthen the manuscript:

1) The results from encoding-retrieval similarity analysis (particularly the one depicted in Figure 3B) don't match the results from encoding/retrieval interaction (particularly those shown in Figure 2C). While they were certainly based on different comparisons, I would think that both analyses were set up to test for memory updating. Can the authors comment on this divergence in results?

Thank you for your comment. Except for one ROI, the other two regions in Figure 2C are present in the interaction analysis. The ROI at the frontal pole might be hard to see from this angle but in fact it holds a high effect size in interaction analysis. So we do not see a big divergence between these two results. But taking into account the recall-recall results, we agree that there seems to be inhomogeneity. We discussed these further in the discussion.

"We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

Our findings are consistent with the view that DMN synthesizes incoming information with one’s prior beliefs and memories (Yeshurun et al 2021). We add to this framework by providing evidence for the involvement of DMN regions in updating prior beliefs in light of new knowledge. Across our different encoding and recall analyses, we observe memory updating effects in a varied subset of DMN regions that do not cleanly map onto a specific subsystem of DMN (Robin and Moscovitch 2017, Ranganath and Ritchey 2012, Ritchey and Cooper 2020). Rather than being divergent, these results might be reflecting inherent differences between the processes of encoding and recall of naturalistic events. It has been proposed that neural representations corresponding to encoding of events are systematically transformed during recall of those events (Chen et al 2017, Favila et al 2020, Musz and Chen 2022). While we provide evidence for reinstatement of memories in DMN, our findings also support a transformation of neural representation during recall, as encoding-recall results were weaker in some areas than recall-recall findings. This transformation could affect how different regions and sub-systems of DMN represent memories, and suggests that the concerted activity of multiple subsystems and neural mechanisms might be at play during encoding, recall and successful updating of naturalistic event memories."

2) The recall task was self-paced. Can reaction time information be provided on how long participants needed to recall? Did this differ across groups? Presumably in the twist group and spoiled group participants might have needed a longer time to incorporate both the original and twist interpretation.

This is an interesting idea. Unfortunately, we could not measure this accurately because our recall cues were snippets from the beginning of each scene with different length (selected based on content). And updating could begin from the beginning of those snippets (but we wouldn’t know when). We will consider this point in the future related designs.

How was the length difference across events taken into consideration in the beta estimates?

They were used as event durations in the GLM model.

Also, is there an order effect, such that one type of interpretation tended to be recalled first?

This is hard to measure as this only occurs in a subset of scenes. But we assume it happens in other people’s brains as well

This is indeed hard to measure as you mentioned. We will provide the transcripts when sharing the data and hopefully this will facilitate future text-analysis work on this dataset to answer interesting questions like this.

3) The correlation analysis between neural pattern change and behavioral twist score is based on a small sample size and does not seem to be well suited to test the postulation of the authors, namely that some participants may hold both interpretations in their memory. Interestingly, the twist score of the spoiled group was similar to the twist group, indicating participants in this group might have held both interpretations as well. Could this observation be leveraged, for example by combining both groups (hence better powered with larger sample size), in order to relate individual differences in neural similarity patterns and behavioral tendency to hold both interpretations?

Even though both groups showed signs of holding both interpretations in mind, the process happening in their brain during the recall is different. In particular, we do not expect to see any updating effect in the spoiled group. So it wouldn’t seem accurate to combine these groups to test the effect of incomplete updating.

4) Several regions within the DMN were significant across the analysis steps, specifically the angular gyrus, middle temporal cortex, and medial PFC. Can the authors provide more insights on how these widely distributed regions may act together to enable memory updating? The discussion on the main findings is largely at a rather superficial level about DMN, or focuses specifically on vmPFC, but neglects the distributed regions that presumably function interactively

Thanks for bringing this up. We added text to discussion to respond to this very valid point. Please see the added text in our response to your first point. One more snippet added to the discussion about this:

"In addition to mPFC, right precuneus and parts of temporal cortex exhibited significantly higher pattern similarity in the “twist” and “spoiled” groups who recalled the movie with the same interpretation. Precuneus is a core region in the posterior medial network, which is hypothesized to be involved in constructing and applying situation models (Ranganath and Ritchey 2012). Our findings support a role for precuneus in deploying interpretation-specific situation models when retrieving event memories. In particular, we suggest that the posterior medial network may encode a shift in the situation model of the “twist” group in order to accommodate the new Ghost interpretation.

We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

Our findings are consistent with the view that DMN synthesizes incoming information with one’s prior beliefs and memories (Yeshurun et al 2021). We add to this framework by providing evidence for the involvement of DMN regions in updating prior beliefs in light of new knowledge. Across our different encoding and recall analyses, we observe memory updating effects in a varied subset of DMN regions that do not cleanly map onto a specific subsystem of DMN (Robin and Moscovitch 2017, Ranganath and Ritchey 2012, Ritchey and Cooper 2020). Rather than being divergent, these results might be reflecting inherent differences between the processes of encoding and recall of naturalistic events. It has been proposed that neural representations corresponding to encoding of events are systematically transformed during recall of those events (Chen et al 2017, Favila et al 2020, Musz and Chen 2022). While we provide evidence for reinstatement of memories in DMN, our findings also support a transformation of neural representation during recall, as encoding-recall results were weaker in some areas than recall-recall findings. This transformation could affect how different regions and sub-systems of DMN represent memories, and suggests that the concerted activity of multiple subsystems and neural mechanisms might be at play during encoding, recall and successful updating of naturalistic event memories."

Reviewer #3 (Public Review):

Zadbood and colleagues investigated the way key information used to update interpretations of events alter patterns of activity in the brain. This was cleverly done by the use of "The Sixth Sense," a film featuring a famous "twist ending," which fundamentally alters the way the events in the film are understood. Participants were assigned to three groups: (1) a Spoiled group, in which the twist was revealed at the outset, (2) a Twist group, who experienced the film as normal, and (3) a No-Twist group, in which the twist was removed. Participants were scanned while watching the movie and while performing cued recall of specific scenes. Verbal recall was scored based on recall success, and evidence for descriptive bias toward two ways of understanding the events (specifically, whether a particular character was or was not a ghost). Importantly, this allowed the authors to show that the Twist group updated their interpretation. The authors focused on regions of the Default Mode Network (DMN) based on prior studies showing responsiveness to naturalistic memory paradigms in these areas and analyzed the fMRI data using intersubject pattern similarity analysis. Regions of the DMN carried patterns indicative of story interpretation. That is, encoding similarity was greater between the Twist and No-Twist groups than in the Spoiled group, and retrieval similarity was greater between the Twist and Spoiled groups than in the No-Twist group. The Spoiled group also showed greater pattern similarity with the Twist group's recall than the No-Twist group's recall. The authors also report a weaker effect of greater pattern similarity between the Spoiled group's encoding and the Twist group's recall than between the Twist group's own encoding and recall. Together, the data all converge on the point that one's interpretation of an event is an important determinant of the way it is represented in the brain.

This is a really nice experiment, with straightforward predictions and analyses that support the claims being made. The results build directly on a prior study by this research group showing how interpretational differences in a narrative drive distinct neural representations (Yeshurun et al., 2017), but extend an understanding of how these interpretational differences might work retrospectively. I do not have any serious concerns or problems with the manuscript, the data, or the analyses. However I have a few points to raise that, if addressed, would make for a stronger paper in my opinion.

1) My most substantive comment is that I did not find the interpretive framework to be very clear with respect to the brain regions involved. The basic effects the authors report strongly support their claims, but the particular contributions to the field might be stronger if the interpretations could be made more strongly or more specifically. In other words: the DMN is involved in updating interpretations, but how should we now think about the role of the DMN and its constituent regions as a result of this study? There are a number of ideas briefly presented about what the DMN might be doing, but it just did not feel very coherent at times. I will break this down into a few more specific points:

While many of us would agree that the DMN is likely to be involved in the phenomena at hand, I did not find that the paper communicated the logic for singularly focusing on this subset of regions very compellingly. The authors note a few studies whose main results are found in DMN regions, but I think that this could stand to be unpacked in a more theoretically interesting way in the Introduction.

Relatedly, I found the summary/description of regional effects in the Discussion to be a bit unsatisfying. The various pattern similarity comparisons yielded results that were actually quite nonoverlapping among DMN regions, which was not really unpacked. To be clear, it is not a 'problem' that the regional effects varied from comparison to comparison, but I do think that a more theoretical exploration of what this could mean would strengthen the paper. To the authors' credit, they describe mPFC effects through the lens of schemas, but this stands in contrast to many other regions which do not receive much consideration.

Finally, although there is evidence that regions of the DMN act in a coordinated way under some circumstances, there is also ample evidence for distinct regional contributions to cognitive processes, memory being just one of them (e.g., Cooper & Ritchey, 2020; Robin & Moscovitch, 2017; Ranganath & Ritchey, 2012). The authors themselves introduce the idea of temporal receptive windows in a cortical hierarchy, and while DMN regions do appear to show slower temporal drift than sensory areas, those studies show regional differences in pattern stability across time even within DMN regions. Simply put, it is worth considering whether it is ideal to treat the DMN as a singular unit.

Thank you for your helpful comments. We added text to the introduction and discussion to address your point:

"Introduction:

The brain’s default mode network (DMN)—comprising the posterior medial cortex, medial prefrontal cortex, temporoparietal junction, and parts of anterior temporal cortex—was originally described as an intrinsic or “task-negative” network, activated when participants are not engaged with external stimuli (Raichle et al. 2001, Buckner et al 2008). This observation led to a large body of work showing that the DMN is an important hub for supporting internally driven tasks such as memory retrieval, imagination, future planning, theory of mind, and creating and updating situation models (Svoboda et al. 2006; Addis et al. 2007; Hassabis and Maguire 2007, 2009; Schacter et al. 2007; Szpunar et al. 2007; Spreng et al. 2009, Koster-Hale & Saxe, 2013 2013, Ranganath and Ritchey 2012). However, it is not fully understood how this network contributes to these varying functions, and in particular—the focus of the present study—memory processes. Activation of this network during “offline” periods has been proposed to play a role in the consolidation of memories through replay (Kaefer et al 2022). Interestingly, prior work has also shown that the DMN is reliably engaged during “online” processing (encoding) of continuous rich dynamic stimuli such as movies and audio stories (Stephens et al 2013, Hasson et al 2008). Regions in this network have been shown to have long “temporal receptive windows” (Hasson et al 2008; Lerner et al., 2011; Chang et al., 2022), meaning that they integrate and retain high-level information that accumulates over the course of extended timescales (e.g. scenes in movies, paragraphs in text) to support comprehension. This combination of processing characteristics suggests that the DMN integrates past and new knowledge, as regions in this network have access to incoming sensory input, recent active memories, and remote long-term memories or semantic knowledge (Yeshurun et al 2021, Hasson et al 2015). These integration processes feature in many of the “constructive” processes attributed to DMN such as imagination, future planning, mentalizing, and updating situation models (Schacter and Addis 2007, Ranganath and Ritchey 2012). Notably, constructive processes are highly relevant to real-world memory updating, which involves selecting and combining the relevant parts of old and new memories. Recent work has shown that neural patterns during encoding and recall of naturalistic stimuli (movies) are reliably similar across participants in this network (Chen et al. 2017; Oedekoven et al., 2017; Zadbood et al., 2017; see Bird 2020 for a review of recent naturalistic studies on memory), and the DMN displays distinct neural activity when listening to the same story with different perspectives (Yeshurun et al 2017). Building on this foundation of prior work on the DMN, we asked whether we could find neural evidence for the retroactive influence of new knowledge on past memories."

"Discussion :

In addition to mPFC, right precuneus and parts of temporal cortex exhibited significantly higher pattern similarity in the “twist” and “spoiled” groups who recalled the movie with the same interpretation. Precuneus is a core region in the posterior medial network, which is hypothesized to be involved in constructing and applying situation models (Ranganath and Ritchey 2012). Our findings support a role for precuneus in deploying interpretation-specific situation models when retrieving event memories. In particular, we suggest that the posterior medial network may encode a shift in the situation model of the “twist” group in order to accommodate the new Ghost interpretation.

We performed two targeted analyses to look for evidence of memory updating across encoding and recall: the interaction analysis (Figure 2C) and the encoding-recall analysis (Figure 3). We hypothesized that a shift in direction of pISC difference would occur when neural representations during recall in the “twist” group start to reflect the Ghost interpretation. The interaction analysis probed this shift indirectly by taking into account the effects of both encoding-encoding and recall-recall analyses. Unlike the interaction analysis, in the encoding-recall analysis, we directly compared neural event representations during encoding and recall. Interestingly, all regions exhibiting an effect across the two encoding-recall analyses, excluding left anterior temporal cortex, were present in the interaction results. Among these regions, the left angular gyrus/TPJ exhibited an effect across all three analyses. As a core hub in the mentalizing network, temporo-parietal cortex has been implicated in theory of mind through perspective-taking, rationalizing the mental state of someone else, and modeling the attentional state of others (Frith and Frith 2006, Guterstam et. al 2021, Saxe and Kanwisher 2003). The motivations behind some actions of the main character in the movie heavily depend on whether the viewer perceives them as a Doctor or a Ghost, and participants may focus on this during both encoding and recall. We speculate that neural event representations in AG/TPJ in the current experiment may be related to mentalizing about the main character’s actions. Under this interpretation, the updated event representations during recall following the twist would be more closely aligned to the “spoiled” encoding representations, as a consequence of memory updating in the “twist” group.

Our findings are consistent with the view that DMN synthesizes incoming information with one’s prior beliefs and memories (Yeshurun et al 2021). We add to this framework by providing evidence for the involvement of DMN regions in updating prior beliefs in light of new knowledge. Across our different encoding and recall analyses, we observe memory updating effects in a varied subset of DMN regions that do not cleanly map onto a specific subsystem of DMN (Robin and Moscovitch 2017, Ranganath and Ritchey 2012, Ritchey and Cooper 2020). Rather than being divergent, these results might be reflecting inherent differences between the processes of encoding and recall of naturalistic events. It has been proposed that neural representations corresponding to encoding of events are systematically transformed during recall of those events (Chen et al 2017, Favila et al 2020, Musz and Chen 2022). While we provide evidence for reinstatement of memories in DMN, our findings also support a transformation of neural representation during recall, as encoding-recall results were weaker in some areas than recall-recall findings. This transformation could affect how different regions and sub-systems of DMN represent memories, and suggests that the concerted activity of multiple subsystems and neural mechanisms might be at play during encoding, recall and successful updating of naturalistic event memories."

2) I think that some direct comparison to regions outside the DMN would speak to whether the DMN is truly unique in carrying the key representations being discussed here. I was reluctant to suggest this because I think that the authors are justified in expecting that DMN regions would show the effects in question. However, there really is no "null" comparison here wherein a set of regions not expected to show these effects (e.g., a somatosensory network, or the frontoparietal network) in fact do not show them. There are not really controls or key differences being hypothesized across different conditions or regions. Rather, we have a set of regions that may or may not show pattern similarity differences to varying degrees, which feels very exploratory. The inclusion of some principled control comparisons, etc. would bolster these findings. The authors do include a whole-brain analysis in Supplementary Figure 1, which indeed produced many DMN regions. However, notably, regions outside the DMN such as the primary visual cortex and mid-cingulate cortex appear to show significant effects (which, based on the color bar, might actually be stronger than effects seen in the DMN). Given the specificity of the language in the paper in terms of the DMN, I think that some direct regional or network-level comparison is needed.

In the original submission, we included additional analyses for visual and somatosensory networks, which we hypothesized would serve as control networks. Following your comment, in the revision, we added a separate section (included below) more thoroughly examining these analyses. We also added text to the results and discussion to explain our interpretation of these findings.

"Changes in neural representations beyond DMN We focused our core analyses on regions of the default mode network. Prior work has shown that multimodal neural representations of naturalistic events (e.g. movie scenes) are similar across encoding (movie-watching or story-listening) and verbal recall of the same events in the DMN (Chen et al., 2017; Zadbood et al., 2017). Therefore, in the current work we hypothesized that retrospective changes in the neural representations of events as the narrative interpretation shifts would be observed in the DMN. We did not, for example, expect to observe such effects in lower-level sensory regions, where neural activity differs dramatically for movie-viewing and verbal recall. To be thorough, we ran the same set of analyses we performed in the DMN (Figure 2-3) in regions of the visual and somatomotor networks extracted from the same atlas parcellation (Schaefer et al., 2018). Our results revealed larger overall differences in DMN than in visual and somatosensory networks for the key comparisons discussed previously (Figure S2). In particular, the only regions showing significant differences in pISC in recall-recall and encoding-recall comparisons (p < 0.01, uncorrected) were located in the DMN. We did not observe a notable difference between DMN and the two other networks when comparing recall “twist” to movie “spoiled” and recall “twist” to movie “twist” (RG – MG > RG – MD) which is consistent with the weak effect in the original comparison (Figure 3B). In the encoding-encoding comparison, several ROIs from the visual and somatomotor networks showed relatively strong effects as well (see Discussion).

In addition, we qualitatively reproduced our results by performing an ROI-based whole brain analysis (Figure S3, p < 0.01 uncorrected). This analysis confirmed the importance of DMN regions for updating neural event representations. However, strong differences in pISC in the hypothesized direction were also observed in a handful of other non-DMN regions, including ROIs partly overlapping with anterior cingulate cortex and dorsolateral prefrontal cortex (see Discussion)."

"Discussion: While our main goal in this paper was to examine how neural representations of naturalistic events change in the DMN, we also examined visual and somatosensory networks. Aside from the encoding-encoding analysis in which some visual and somatosensory regions showed stronger similarity between two groups with the same interpretation of the movie, we did not find any regions with significant effects in these two networks in the other analyses. Unlike the recall phase where each participant has their unique utterance with their own choice of words and concepts to describe the movie, the encoding (move-watching) stimulus is identical across all groups. Therefore, the effects observed during encoding-encoding analysis in sensory regions could reflect similarity in perception of the movie guided by similar attentional state while watching scenes with the same interpretation (e.g. similarity in gaze location, paying attention to certain dialogues, or small body movements while watching the movie with the same Doctor or Ghost interpretations). In our whole brain analysis, these regions did not have significant interaction effects, which suggests that the effects were isolated to encoding. In the whole-brain analysis, we also observed a significant encoding-encoding and interaction effects in anterior cingulate cortex, as well as recall-recall and interaction effects in dlPFC. These results suggest that both the "spoiled" manipulation and the "twist" may recruit top-down control and conflict monitoring processes during naturalistic viewing and recall."

3) If I understand correctly, the main analyses of the fMRI data were limited to across-group comparisons of "critical scenes" that were maximally affected by the twist at the end of the movie. In other words, the analyses focused on the scenes whose interpretation hinged on the "doctor" versus "ghost" interpretation. I would be interested in seeing a comparison of "critical" scenes directly against scenes where the interpretation did not change with the twist. This "critical" versus "non-critical" contrast would be a strong confirmatory analysis that could further bolster the authors' claims, but on the other hand, it would be interesting to know whether the overall story interpretation led to any differences in neural patterns assigned to scenes that would not be expected to depend on differences in interpretation. (As a final note, such a comparison might provide additional analytical leverage for exploring the effect described in Figure 3B, which did not survive correction for multiple comparisons.)

This is a helpful suggestion, and we’ve added an analysis addressing your comment. We found that the interaction index capturing the difference between the three groups was stronger for the critical scenes than for the non-critical scenes for almost all DMN ROIs.

"The role of scene content In the prior analyses, we focused on “critical scenes”, selected based on ratings from four raters who quantified the influence of the twist on the interpretation of each scene (see Methods). An independent post-experiment analysis of the verbal recall behavior of the fMRI participants yielded “twist scores” that were also highest for these scenes; that is, the expected and perceived effect of twist information on recall behavior were found to match. In our next analysis, we asked whether the neural event representations reflect these differences in the twist-related content of the scenes. In other words, are the “critical scenes” with highly twist-dependent interpretations truly critical for our observed effects?

To answer this question, we re-ran our main encoding-encoding and recall-recall pISC analysis in each DMN ROI (Figure 2-3). We calculated interaction indices (Figure 2C) first by including all scenes, and second by including only the 11 non-critical scenes. To better compare the effect of including different subsets of scenes to our original results, in Figure 4 we show the results in 15 ROIs that exhibited meaningful effects in our main analyses (Figure 2C). Figure 4A demonstrates that “critical scenes” yielded higher interaction indices compared to all scenes or non-critical scenes across all ROIs. The interaction score across all DMN ROIs was significantly higher in “critical scenes” than all scenes (t(23) = 7.19, p = 2.53 x 10-7) and non-critical scenes (t(23) = 7.3, p = 1.95 x 10-7). These results show that critical scenes are indeed responsible for the observed pISC differences across groups."

4) I appreciate the code being made available and that the neuroimaging data will be made available soon. I would also appreciate it if the authors made the movie stimulus and behavioral data available. The movie stimulus itself is of interest because it was edited down, and it would be nice for readers to be able to see which scenes were included.

Unfortunately due to copyright, we cannot share the movie stimulus outright. However, we will share the timing of the cuts used, as well as the time-stamped transcripts of verbal recall.

To sum up, I think that this is a great experiment with a lot of strengths. The design is fairly clean (especially for a movie stimulus), the analyses are well reasoned, and the data are clear. The only weaknesses I would suggest addressing are with regards to how the DMN is being described and evaluated, and the communication of how this work informs the field on a theoretical level.

Author Response

Reviewer #1 (Public Review):

In a very interesting and technically advanced study, the authors measured the force production of curved protofilaments at depolymerizing mammalian microtubule ends using an optical trap assay that they developed previously for yeast microtubules. They found that the magnesium concentration affects this force production, which they argue based on a theoretical model is due to affecting the length of the protofilament curls, as observed previously by electron microscopy. Comparing with their previous force measurements, they conclude that mammalian microtubules produce smaller force pulses than yeast microtubules due to shorter protofilament curls. This work provides new mechanistic insight into how shrinking microtubules exert forces on cargoes such as for example kinetochores during cell division. The experiments are sophisticated and appear to be of high quality, conclusions are well supported by the data, and language is appropriate when conclusions are drawn from more indirect evidence. Given that the experimental setup differs from the previous optical trap assay (antibody plus tubulin attached to bead versus only antibody attached to bead), a control experiment could be useful with yeast microtubules using the same protocol used in the new variant of the assay, or at least a discussion regarding this issue. One open question may be whether the authors can be sure that measured forces are only due to single depolymerizing protofilaments instead of two or more protofilaments staying laterally attached for a while. How would this affect the interpretation of the data?

This work will be of interest to cell biologists and biophysicists interested in spindle mechanics or generally in filament mechanics.

Thank you for your careful reading of our manuscript, your kind remarks, and your favorable review.

Reviewers #1 and #2 both mentioned a concern about potential differences between our previous setup with yeast microtubules, versus our new setup with predominantly bovine microtubules, and whether such differences might underlie the different pulse amplitudes we measured. We think this concern comes mainly from a misunderstanding of how the beads in both setups were tethered to the sides of the microtubules, and we apologize for not making this aspect clearer in our original submission.

It is true that our new setup requires one additional step, pre-decoration of the anti-His beads with His6-tagged yeast tubulin. However, in both cases, the anti-His antibodies were kept very sparse on the beads to ensure that most beads, if they became tethered to a microtubule, were attached by a single antibody. (~30 pM beads were mixed with 30 pM of anti-His antibody, for a molar ratio of 1:1.) And even though the anti-His beads in our previous work did not undergo a separate incubation step for pre-decoration with tubulin, they undoubtedly were decorated immediately after being mixed into the microtubule growth mix, which in that case included ~1 µM of unpolymerized His6-tagged yeast tubulin dimers. Thus, the arrangement with beads tethered laterally to the sides of microtubules via single antibodies was created in both cases by essentially the same three-step process: First, beads decorated very sparsely with anti-His antibodies were bound to unpolymerized His6-tagged yeast tubulin. Second, a bead-tethered His6-tagged yeast tubulin was incorporated into the growing tip of a microtubule (which could be assembling from either yeast or bovine tubulin, depending on the experiment). Third, the tip grew past the bead to create a large extension. Because the beads in both scenarios were tethered by a single antibody to the same C-terminal tail of yeast β-tubulin, the differences in pulse amplitude cannot be explained by differences in the tethering. In our revised manuscript, we now mention explicitly in Results that the beads were tethered by single antibodies (lines 95 to 100). In Methods we significantly expanded the section about preparation of beads and how they became tethered (lines 365 to 393). [We refer here, and below, to line numbers when the document is viewed with “All Markup” shown.]

You also raise an interesting, open question: Do protofilaments curl outward entirely independently of their lateral neighbors? Or under some conditions might they tend to stay laterally associated during the curling process, perhaps curling outward in pairs rather than as individual protofilaments? We cannot formally rule out the possibility that such lateral associations sometimes persist during protofilament curling. However, changes in lateral association seem unlikely to explain the magnesium- and species-dependent differences we measured in pulse amplitude, for several reasons: First, there is good evidence for lengthening of protofilament curls at disassembling tips (e.g., Mandelkow 1991, Tran & Salmon 1997), but we are not aware of convincing evidence for magnesium or species-dependent increases in the propensity of curling protofilaments to remain laterally associated. Second, an increase in lateral association should increase the effective flexural rigidity of the curls, but under all the conditions we examined, pulse enlargement was associated with a steepening of the amplitude-vs-force relation – i.e., with softening, not stiffening. Our model indicates that this softening can be fully explained by an increase in protofilament contour length, without any change in the intrinsic flexural rigidity of the protofilament curls.

Reviewer #2 (Public Review):

Microtubules are regarded as dynamic tracks for kinesin and dynein motors that generate force for moving cargoes through cells, but microtubules also act as motors themselves by generating force from outward splaying protofilaments at depolymerizing ends. Force from depolymerization has been demonstrated in vitro and is thought to contribute to chromosome movement and other contexts in cells. Although this model has been in the field for many years, key questions have remained unanswered, including the mechanism of force generation, how force generated might be regulated in cells, and how this system might be tuned across cellular contexts or organisms. The barrier is that we lack an understanding of experimental conditions that can be used to control protofilament shape and energetics. This study by Murray and colleagues makes an important advance towards overcoming that barrier.

This study builds on previous work from the authors where they developed a system to directly measure forces generated by outward curling protofilaments at depolymerizing microtubule ends. That study showed for the first time that protofilaments act like elastic springs and related the generated force to the estimated energy contained in the microtubule lattice. Furthermore, they showed that slowing polymerization rate did not diminish force generation. That study used recombinant yeast tubulin, including a 6x histidine tag on beta tubulin that created attachment points for the bead on the microtubule lattice. The current study extends that system to show that work output is related to the length of protofilament curls.

We are grateful for your very thoughtful and thorough review, which has helped us improve our manuscript.

Murray and colleagues show this by manipulating curls in two ways - using bovine brain tubulin instead of yeast tubulin and altering magnesium concentration. Previous EM studies indicated that protofilaments on depolymerizing bovine microtubules have similar curvature but are shorter. The authors here use a blend of bovine brain tubulin and bead-linked recombinant yeast tubulin with the 6x histidine tag in their in vitro system and find smaller deflections of the laser-trapped bead than previously observed with pure yeast tubulin. A concern with comparing this heterogeneous bovine/yeast system to the previous work with homogeneous yeast tubulin is that density of 6x histidine-tagged tubulin subunits is likely to be different between the two systems. Also, the rate of incorporation of 6x histidine yeast tubulin into bovine microtubules in the current study may be different from the rate of incorporation into yeast microtubules in the previous study. These differences could lead to changes in the strength of bead attachment to the microtubule lattice and alter the compliance of the bead to deflection by curling protofilaments. These possibilities and lattice attachment strength are not explored in this study, raising concerns about comparing the two systems.

Reviewers #1 and #2 both mentioned a concern about potential differences between our previous setup with yeast microtubules, versus our new setup with predominantly bovine microtubules, and whether such differences might underlie the different pulse amplitudes we measured. As detailed in our response to Reviewer #1 above, we think this concern comes mainly from a misunderstanding of how the beads in both setups were tethered to the sides of the microtubules, and we apologize for not making this aspect clearer in our original submission. For both our yeast and bovine microtubule experiments, the anti-His antibodies were kept very sparse on the beads to ensure that most beads, if they became tethered to a microtubule, were attached by a single antibody. Because the beads in both scenarios were tethered by a single antibody to the same C-terminal tail of yeast β-tubulin, the differences in pulse amplitude cannot be explained by differences in the tethering. In our revised manuscript, we now mention explicitly in Results that the beads were tethered by single antibodies (lines 95 to 100). In Methods we significantly expanded the section about preparation of beads and how they became tethered (lines 365 to 393).

The authors go on to show that magnesium increases bead deflection and work output from the system. The use of magnesium was motivated by earlier studies which showed that increasing magnesium speeds up depolymerization and increases the lengths of protofilament curls. The use of magnesium here provides the first evidence that work output can be tuned biochemically. This is an important finding. The authors then go on to show that the effect of magnesium on bead deflection can be separated from its effect on depolymerization speed. They do this by proteolytically removing the beta tubulin tail domain, which previous studies had shown to be necessary to mediate the magnesium effect on depolymerization rate. The authors arrive at a conclusion that magnesium must promote protofilament work output by increasing their lengths. How magnesium might do this remains unanswered. The mechanistic insight from the magnesium experiments ends there, but the authors discuss possible roles for magnesium in strengthening longitudinal interactions within protofilaments or perhaps complexing with the GDP nucleotide at the exchangeable site, although that seems less likely at the concentrations in these experiments.

The major conclusion of the study is the finding that work output from curling protofilaments is a tunable system. The examples here demonstrate tuning by tubulin composition and by divalent cations. Whether these examples relate to tuning in biological systems will be an important next question and could expand our appreciation for the versatility of depolymerizing microtubules as a motor.

We fully agree that two very important next questions are whether work output from curling protofilaments is truly harnessed in vivo, and whether protofilament properties in vivo might be actively regulated for this purpose. Based on your recommendations, and as detailed below (under Major point 2), we have expanded our discussion of these possibilities in our revised manuscript.

Reviewer #3 (Public Review):

The authors used a previously established optical tweezers-based assay to measure the regulation of the working stroke of curled protofilaments of bovine microtubules by magnesium. To do so, the authors improved the assay by attaching bovine microtubules to trapping beads through an incorporated tagged yeast tubulin.

The assay is state-of-the-art and provides a direct measurement of the stroke size of protofilaments and its dependence on magnesium.

The authors have achieved all their goals and the manuscript is well written.

The reported findings will be of high interest for the cell biology community.

Thank you for reading and evaluating our manuscript. We are grateful for your positive comments.

Author Response

Reviewer #1 (Public Review):

The authors found that the IDR in Cdc15 gets phosphorylated by multiple kinases, Pom1/Shk1/Pck1/Kin1, and the phosphorylation on IDR inhibits the phase separation of the Cdc15 protein. The phosphorylation was demonstrated in the cell as well as in vitro. Moreover, the phosphorylation sites were identified by mass spectrometry. The phospho-regulation of Cdc15 LLPS was demonstrated by in vitro assay using recombinant proteins. The significance of the phosphorylation on contractile actomyosin ring (CAR) was demonstrated by using a cdc15 mutant carrying 31 Ala-substitutions at the phosphorylation sites (cdc15 31A). The CAR assembled comparable to cdc15+, but maturation and contraction of the ring were faster in the cdc15 31A mutant, suggesting the contribution of the phosphorylation for delaying cytokinesis. This could be one of the mechanisms to ensure the completion of chromosome segregation before the cytokinesis. In this paper, the authors showed over-accumulation of type-II myosin regulatory light chain Rlc1 on CAR in the cdc15 31A mutant during the CAR assembly and its contraction. In addition, the kinases for the Cdc15 IDR phosphorylation are identified as polarity kinases, which restrict the assembly of the CAR formation in the middle. Indeed, inhibition of the kinases increases the ratio of septa formation at the cell tip in the mid1 knockout mutant, which lacks a major positive polarity cue during the mitotic phase. However, in this manuscript, this phenotype is not solely explained by the phosphorylation of the cdc15 31A, because the authors did not show the tip septa formation using cdc15 31A.

Preventing Cdc15 phosphorylation does not on its own promote tip septa formation (Bhattacharjee et al., 2020). The polarity kinases have other substrates in the tip exclusion pathway that presumably also play a key role in septation. Also, cells must also be in the correct part of the cell cycle to form functional CRs and septa. We described the necessary roles of other polarity kinase substrates in our discussion.

Overall, the data supports their conclusion, Cdc15 forms LLPS, and the process is inhibited by the phosphorylation of amino acid residues in the IDR in Cdc15 by polarity kinases. It is still unclear whether LLPS formation is a reversible process regulated by the protein kinases. In vitro experiments showed condensate formation by dephosphorylation of Cdc15 IDR but not diffusion of the LLPS by phosphorylation. I wonder if incubation of the kinases and the Cdc15 IDR condensates induces demolition of the LLPS.

This is an interesting idea but technically challenging. The reactions performed in vitro are done by adding phosphatase to induce droplet formation and there is no way to remove the phosphatase. Therefore, addition of kinase will battle the phosphatase and clear results are unlikely. What we do know from work in vivo is that without the ability to rephosphoryate Cdc15 with the Alanine mutants, the protein remains bound to membrane in clusters so it seems clear that it is the phosphostate of Cdc15 that governs this property of the protein.

The transition of the Cdc15 IDR phosphorylation and LLPS formation through the cell cycle progression is unclear. In asynchronous cells (most of the cells may be in the G2 phase) and nda3 or cps1 mutants, Cdc15 was still highly phosphorylated. This indicates that the Cdc15 is phosphorylated and the LLPS formation is inhibited throughout the cell cycle. The transition of the phosphorylation status for individual residues could be the next challenge for this research.

The cell cycle changes in Cdc15 phosphostatus and their correlation with localization have been well-documented (e.g. Fankhauser et al., Cell, 1998; Clifford et al., JCB, 2008; Roberts-Galbriath et al., Mol. Cell, 2010). Upon bulk analysis, Cdc15 is never fully dephosphorylated during mitosis but it is not highly phosphorylated in cells blocked in mitosis with nda3 or in cps1 cells when some portion of it is in CRs (please see the references indicated previously). As shown in the simulations, the protein need not be fully phosphorylated or dephosphorylated in order to undergo a conformational change that would allow condensate formation. A major conclusion of our work is that no particular phosphorylation site or sites is important but rather the overall charge on the dimer is important and that some threshold of phosphorylation keeps the protein off from forming clusters on the membrane. We agree with the reviewer that what that threshold is will be of interest in the future.

In addition, currently, there is no approach to monitor the LLPS in wild-type cells. Therefore, it is still unclear if LLPS formation is the physiological mechanism regulating cell division in wild-type cells.

We agree that we have not monitored LLPS in live cells. However, Cdc15’s condensate formation in live cells and its phosphorylation state are highly correlated. This suggestive of LLPS in vivo.

Author Response

Reviewer #2 (Public Review):

“To describe LLPS or to distinguish between polymer-polymer phase separation and LLPS, recent studies have used single particle tracking, a technique allowing to follow the dynamics of individual proteins in living cells (https://doi.org/10.7554/eLife.60577; https://doi.org/10.7554/eLife.69181; https://doi.org/10.7554/eLife.47098). The authors should mention that such an approach can be a good alternative to avoid the artefact of fixation. Using techniques such as single particle tracking or FCS, it is possible to estimate the effective diffusion coefficient of protein-living cells. When a liquid phase separation is formed, it is also possible to estimate the diffusion coefficient of the protein of interest (POI) inside versus outside of the LLPS.”

We thank the reviewer for their insight and fully agree that live-cell techniques like SPT and FCS are valuable for investigating LLPS while avoiding fixation artifacts. We have added discussion emphasizing this fact and incorporated the citations recommended by the reviewer in Paragraph 1 on Page 15: “Live imaging techniques that allow estimation of protein diffusion coefficients within specific cellular compartments, e.g., SPT (Hansen et al., 2018 and Heckert et al., 2022) and fluorescence correlation spectroscopy (Lanzanò et al., 2017), can be useful alternative approaches for diagnosing LLPS in vivo without the potential artifact of fixation, as diffusion dynamics are recently shown to be affected by LLPS (Heltberg et al., 2021; McSwiggen et al., 2019a; Miné-Hattab et al., 2021; Chong et al., 2022; and Ladouceur et al., 2020).”

“The authors say that less dynamic interactions are better captured by PFA fixation. In the simulation part, would it be possible to predict from the diffusion coefficients of the POI inside a condensate the effect of the PFA fixation? […] In the simulation part, they could try to incorporate the diffusion coefficient of the protein of interest and see if it is possible to predict the effect of fixation as a function of the diffusion coefficient.”

We thank the reviewer for pointing out the absence of this critical piece that connects our experimental observations to our kinetic model. Our model considers association/dissociation rates rather than diffusion coefficients to describe interaction dynamics, but the reviewers’ point is still very insightful and important. As described in Response 2, we compared two proteins: Halo-TAF15(IDR), which is poorly preserved by fixation, and TAF15(IDR)-Halo-FTH1, which is well preserved by fixation. We used SPT to measure the dissociation rates of Halo-TAF15(IDR) and TAF15(IDR)-Halo-FTH1 and showed that the dissociation rate of Halo-TAF15(IDR) from its puncta is much faster than that of TAF15(IDR)-Halo-FTH1, demonstrating more stable homotypic interactions of the latter than the former. The observation that TAF15(IDR)-Halo-FTH1 has less dynamic interactions and is better preserved by fixation compared to Halo-TAF15(IDR) agrees with our model’s prediction that less dynamic interactions are better captured by fixation. Please see Response 2 for more details. Our new data and discussion have been added to the revised manuscript in Paragraph 3 on Page 13 and in Figure 3B, Figure 3E, Figure 6, and Video 2.

“Finally, the authors propose that in the future, it will be important to design novel fixatives with significantly faster cross-linking rates than biomolecular interactions to eliminate fixation artifacts in the cell. It would be even more interesting if the authors could propose some ideas of potential novel fixatives. Did they test several concentrations of PFA, for example? Did they test different times of PFA incubation? Did they test cryofixation and do they know what would be their effect on LLPS? Do they have novel fixatives in mind? […] To strengthen the manuscript, the authors should try more protocols of fixation.”

We thank the reviewer for these good questions. As described in Response 1, we have done additional quantification of the change of LLPS appearance in cells upon treatment of 0% PFA (only PBS buffer), 1% PFA, 2% PFA, and 8% PFA as well as 4% PFA supplemented by 0.2% GA. We saw statistically significant changes in the LLPS-describing parameters upon all the PFA and PFA/GA treatments except the 0% PFA control. To examine how fixation artifacts depend on the time of PFA incubation, we acquired a time-lapse movie of a cell overexpressing EGFP-FUS(IDR) immediately after 4% PFA treatment and quantified the number of puncta over time (Video 1). We showed that fixation is complete (the number of puncta becomes constant) by roughly 100 seconds (Figure 1 – figure supplement 2). Our new data also justified our choice of a 10-minute PFA incubation time for analyzing fixation-induced change of LLPS appearance in the rest of the paper. Please see Response 1 for more details. Our new data and discussion have been added to the revised manuscript in Paragraph 3 on Page 3 and in Figure 1 - figure supplement 2 (time dependence of fixation artifacts), Figure 1 - figure supplement 3 (fixation artifact at various PFA concentrations), and Figure 1 - figure supplement 4 (fixation artifact upon treatment of 4% PFA supplemented with 0.2% GA).

We agree that testing more cell fixation protocols such as cryofixation on LLPS appearance would be interesting. However, given the complexity of novel fixation protocols like cryofixation and highly specialized equipment and reagents they require, testing widely how different fixation methods might change LLPS appearance would be a tremendous amount of work that is enough to fill a separate paper. These experiments would be much more appropriate for a separate study in the future.

Reviewer #3 (Public Review):

“Understanding whether/how fixation methods affect the detection of biomolecular condensates is of broad interest given the importance of LLPS in regulating different aspects of cell biology. However, in this manuscript, the authors use only paraformaldehyde as a fixation method and study only fluorescently-labelled IDR proteins. The work would benefit from a comparison between living cells and cells fixed with other fixation methods.”

We appreciate the reviewer for this suggestion and agree that more fixation protocols should be investigated. As described in Response 1 and Response 18, besides examining PFA fixation, we have quantified how fixation using 4% PFA supplemented by 0.2% GA changes LLPS appearance in cells. We saw statistically significant changes in all the LLPS-describing parameters upon PFA/GA treatments. Please see Response 1 and Response 18 for details. Our new data and discussion have been added to the revised manuscript in Paragraph 3 on Page 3 and in Figure 1 - figure supplement 4.

“In addition, it would be useful to test the impact of these fixation methods on the detection of endogenous proteins or IDR proteins without fluorescent tag.”

We appreciate the reviewer for this suggestion and have now investigated an endogenous IDR-containing protein in the revised manuscript. Specifically, we quantified the effect of 4% PFA fixation on endogenously expressed EWS::FLI1 in an Ewing sarcoma cell line A673, which is an oncogenic fusion transcription factor that causes Ewing sarcoma (Grünewald et al., 2018) and known to form local, high-concentration hubs at target genes associated with GGAA microsatellites (Chong et al., 2018). We previously Halo-tagged endogenous EWS::FLI1 in A673 cells using CRISPR/Cas9-mediated genome editing (Chong et al., 2018). Here, we quantified the effect of PFA fixation on endogenous EWS::FLI1 puncta in this knock-in cell line and found no significant difference in the distribution of EWS::FLI1 upon fixation. This result suggests that PFA fixation does not change the intracellular distribution of all proteins. Our new data and discussion have been added to the revised manuscript in Paragraph 1 on Page 8 and in Figure 3C.

Unfortunately, testing fixation artifacts of IDR-containing proteins without a fluorescent tag has been infeasible as we rely on fluorescence from a tag on the protein of interest to quantitatively compare LLPS appearance in live and fixed cells. Although we have considered using non-fluorescent methods, e.g., phase contrast microscopy, to visualize putative LLPS in cells, its lack of specificity in imaging proteins or cellular structures makes the type of quantification we do for fixation artifact characterization inaccessible.

Author Response

Reviewer #1 (Public Review):

1 - Problems with the analysis of stimulation latency

The data in this paper show a variable latency in signal propagation from stimulation sites to hippocampal recording electrodes. In an attempt to measure this latency, the authors examine the theta phase offset between each pair of stimulation and recording electrodes (Figure 9). They interpret their results as showing a consistent 90-degree phase offset. However, their data do not support this interpretation because in fact their measurements show a bimodal distribution of phase differences with peaks at 0 and 180 degrees. It is not valid to interpret the circular mean of a bimodal distribution because the result is not well defined. Further, individual electrodes do not show a mean difference of 90 degrees.

Because the results do not reliably support the claim of a consistent 90 phase difference between the hippocampus and cortex, it is a substantial problem for the paper, given the importance of hippocampal-cortical timing in their interpretation. In particular, the authors should reconsider how they frame their results in relation to the Siegle and Wilson work and others.

We no longer emphasize the phase difference between hippocampus and neocortex in the revised manuscript. This phase difference was computed to attempt to address the possibility that there was some latency in the propagation of stimulation effects from lateral temporal cortex to hippocampus, which would affect our interpretation of which theta phase angles evoked minimal versus maximal hippocampal response (i.e., “peak” stimulation trials may actually have involved stimulation propagating to hippocampus sometime after its peak). However, as noted above in response to Essential Revisions #1, we cannot fully rule out the possibility that volume conduction influenced our estimates of phase lag. We no longer emphasize this analysis and have moved it to the appendix (Appendix 1-Figure 4), along with a new analysis using bipolar rereferencing to address the volume conduction issue.

The manuscript is now focused on the main finding of the experiment, of a 180-degree separation between theta phases associated with minimal versus maximal evoked responses. We analyzed this via circular-linear models of phase versus evoked amplitude, as suggested by the reviewers, rather than the phase-binning analyses emphasized in the original manuscript. Circular-linear analyses are indifferent to the specific phase values associated with minimal/maximal response. We have also expanded our Introduction with further discussion of homologies to the rodent literature, including to the Siegle and Wilson paper. Our revised Discussion section emphasizes that the central homology is that there is 180-degree separation between hippocampal theta phase angles associated with minimal versus maximal responsiveness to input, with less emphasis placed on the specific angles (i.e., peak versus trough), given difficulties in comparing specific phase angles across species and recording approaches.

2 - Problems with the figures

Some figures in the paper were hard to interpret and I felt it would benefit readers for many to be combined. The results from Figures 3 through 7 would be helpful to see side by side, as they show various investigations of the same data. In Figure 4, it would be helpful to see both plots from (a) on the same axis, as is in (b). I did not find that the accuracy estimation paper in Figure 2 was important to include in the main paper. It would be better suited for the supplement, in my view, unless I am missing something.

We have substantially revised the figures for clarity. The analyses presented in original Figures 2, 6, and 9 have been moved to the appendix (as revised Appendix Figures 1, 3, and 4). Figure 3 has been combined with Figure 1 into the revised Figure 1. Figures 4 and 7 have been combined in order to show EP data from all four phase bins side-by-side (Figure 3). We did not combine a) and b) from the original figure onto the same axis, as we found it difficult to interpret the four overlaid traces (i.e., 2 EP traces and 2 phase-matched stimulation-free traces). However, these data are now shown side-by-side and on equal axes. We have updated all EP visualizations to improve readability. Figure 5 has been expanded to include component amplitudes comparisons for both peak versus trough and rising versus falling phases, in keeping with the expanded Figure 3.

Author Response

Reviewer #2 (Public Review):

This clinical trial is conducted to pursue short course DAA therapy. For an ultra-short course to work, it has to be simple, equally efficacious to established treatments, and requires no additional workup (like genotyping, IL28B, HCV VL determination, etc after initiation of therapy as shown in Liu et al.). This is because our aim is to simplify therapy to treat most people, especially those who are not engaged in care. This work struggles to achieve these goals, as the to the SVR for short-course therapy is unacceptably low. The authors' conclusion that treat short first and then you can treat those who fail again does not appear to achieve these goals, as realistically,it is difficult to re-engage marginalized population from an elimination perspective. The ideal is to treat them in one attempt.

We would like to clarify that we do not propose treating with 4 weeks and then retreating, because we acknowledge an unacceptable first line cure rate with this approach. We suggest 8 weeks may achieve cure rate of greater than 90% in mild liver disease (18/18 participants with slow virological response were cured with 8 weeks SOF/DCV in this study). Since retreatment with the same drug combination is effective, there is arguably less jeopardy in a regimen with 90% cure rate than previously perceived.

Reviewer #3 (Public Review):

This prospective study evaluated the utility of D2 VL determination for response-guided ultra-short (4w) sofosbuvir + daclatasvir treatment of chronic HCV patients (with mild disease) with G1+6. Shortening therapy duration reduces DAA use with a cure rate of 75% overall upon first-line treatment and 100% among retreated patients. In contrast to a previous report in G1b patients that showed a 100% success rate with D2-based 3-week triple therapy, the present study fails to show a good enough yield for a 4w sofosbuvir + daclatasvir regimen among G1+6 patients. Given the small number of patients, additional studies should determine whether a different time point and/or a different viral threshold could be more appropriate indicators to allow a 4-week duration of dual therapy (without a protease inhibitor).

Strengths:

A) An important study that is a nice addition to previous reports evaluating the utility of response-guided therapy for shortening the duration of HCV treatment. Given the disease burden and the high costs of treatment, especially in low-income countries, this is a major goal that was also advocated by the WHO.

B) This study investigates an ultra-short protease-inhibitor-free regimen and therefore complements a previous (positive) RGT study of a 3-week triple regimen.

C) This study is prospective with careful analyses of ample data, including the evaluation of RAS by gene sequencing. The follow-up was long enough and analyses of viral kinetics were performed. In addition, a detailed analysis of re-treatment outcomes and viral mutations in this population was performed

D) Although the main objective (shortening therapy to 4 weeks) was not adequately achieved (<90% success rate), the study's results may suggest that re-treatment in case of failure is safe and efficient, although further studies with a higher number of patients are needed for confirmation.

Limitations:

A) Relatively small study cohort. Overall, only 34 patients were treated with a 4-week regimen. However, given the results, it seems that this number of patients who achieved only a 75% cure rate, is enough to exclude the use of a D2 RGUT, at least in G1+6 patients treated with sofosbuvir + daclatasvir. On the other hand, even 100% of success rate on 8-week treatment among 17 patients is not really enough to draw firm conclusions on the adequacy of this short regimen among this group of patients. A higher number of patients could better validate this positive result.

Addressed in discussion. Firstly, it was powered to determine overall cure rate with 4- and 8- weeks treatment, rather than outcomes with each duration. It is possible that we would have seen patients failing 8 weeks therapy with a larger sample, and our cure estimates may therefore be imprecise.

B) The values chosen for the RGT are arbitrary. The relatively small number of patients could not allow for a more detailed analysis of more appropriate time points and/or viral load thresholds to determine the adequacy of a 4-week of therapy in individual patients. The D2 500IU/ML threshold is based on a small previous phase 2 study on G1b patients treated with a triple-drug regimen, which does not necessarily imply dual therapy (w/o a protease inhibitor) involving patients with a different subtype of the virus. In this context, a control group treated with triple combination therapy (with a protease inhibitor) could be very helpful to the study.

This was a mechanistic pilot study conducted in Vietnam, where antiviral options are limited. We therefore made a conscious decision to use licensed/available treatments (SOF/DCV) rather than Lau combination which is not WHO-approved.

C) Is there a particular pattern of viral kinetics to 4w cured patients Vs. failures? Fig 1 (Appendix 1) only shows the means of viral load and the general kinetics for the whole population, but individual plots of viral kinetics are not presented although could potentially be useful. Also, according to the presented data, day 7 VL<LLOQ may be a better indicator for shortening treatment to 4w. A detailed graphical presentation of viral kinetics in these patients could be helpful.

We have added appendix 1- figure 2 showing HCV RNA kinetics in participants treated with 4 weeks SOF/DCV, with cures (red lines) distinguished from treatment failures. In results section we comment on this that Even though the numbers are small, this helps illustrate that early on-treatment response alone may be of limited value in determining cure with ultra-short therapy.

D) According to Table 3, no significant differences in the host or viral factors were detected between cured or failures of the 4w regimen. However, the low number of patients makes it very difficult to interpret these data and might miss potential differences between these two groups of patients, emphasizing again the difficulty in drawing firm conclusions from this study. In this context, I wonder whether a regression analysis would better define either viral (subtype, RAS) or host factors that are implicated in a 4w duration success.

See above.

Author Response

Reviewer #1 (Public Review):

Auwerx et al. have taken a new approach to mine large existing datasets of intermediary molecular data between GWAS and phenotype, with the aim of uncovering novel insight into the molecular mechanisms which lead a GWAS hit to have a phenotypic effect. The authors show that you can get additional insight by integrating multiple omics layers rather than analyzing only a single molecular type, including a handful of specific examples, e.g. that the effect of SNPs in ANKH on calcium are mediated by citrate. Such additional data is necessary because, as the authors' point out, while we have thousands of SNPs with significant impact on phenotypes of interest, we often don't know at all the mechanism, given that the majority of significant SNPs found through GWAS are in non-coding (and often intergenic) regions.

This paper shows how one can mine large existing datasets to better estimate the cellular mechanism of significant, causal SNPs, and the authors have proven that by providing insight into the links between a couple of genes (e.g. FADS2, TMEM258) and metabolite QTLs and consequent phenotypes. There is definitely a need and utility for this, given how few significant SNPs (and even fewer recently-discovered ones) hit parts of the DNA where the causal mechanism is immediately obvious and easily testable through traditional molecular approaches.

I find the paper interesting and it provides useful insight into a still relatively new approach. However, I would be interested in knowing how well this approach scales to the general genetics community: would this method work with a much smaller N (e.g. n = 500)? Being able to make new insights using cohorts of nearly 10,000 patients is great, but the vast majority of molecular studies are at least an order of magnitude smaller. While sequencing and mass spectrometry are becoming exponentially cheaper, the issue of sample size is likely to remain for the foreseeable future due to the challenges and expenses of the initial sample collection.

We thank the reviewer for his assessment and have now addressed – in the revised version of the manuscript, as well as in the below point-by-point reply – his specific comments/questions.

Reviewer #2 (Public Review):

Auwerx et al. present a framework for the integration of results from expression quantitative trait loci (eQTL), metabolite QTL (mQTL) and genome-wide association (GWA) studies based on the use of summary statistics and Mendelian Randomization (MR). The aim of their study is to provide the field with a method that allows for the detection of causal relationships between transcript levels and phenotypes by integrating information about the effect of transcripts on metabolites and the downstream effect of these metabolites on phenotypes reported by GWA studies. The method requires the mapping of identical SNPs in disconnected mQTL and eQTL studies, which allows MRbased inference of a causal effect from a transcript to a metabolite. The effect of both transcripts and metabolites on phenotypes is evaluated in the same MR-based manner by overlaying eQTL and mQTL SNPs with SNPs present in phenotypic GWA studies.

The aim of the presented approach is two-fold: (1) to allow identification of additional causal relationships between transcript levels and phenotypes as compared to an approach limited to the evaluation of transcript-to-phenotype associations (transcriptome-wide MR, TWMR) and (2) to provide information about the mechanism of effects originating from causally linked transcripts via the metabolite layer to a phenotype.

The study is presented in a very clear and concise way. In the part based on empirical study results, the approach leads to the identification of a set of potential causal triplets between transcripts, metabolites and phenotypes. Several examples of such causal links are presented, which are in agreement with literature but also contain testable hypotheses about novel functional relationships. The simulation study is well documented and addresses an important question pertaining to the approach taken: Does the integration of mQTL data at the level of a mediator allow for higher power to detect causal transcript to phenotype associations?

We thank the reviewer for his/her assessment and have now addressed – in the revised version of the manuscript, as well as in the below point-by-point reply – his/her specific comments/questions.

Major Concerns

1) Our most salient concern regarding the presented approach is the presence of multiple testing problems. In the analysis of empirical datasets (p. 4), the rational for setting FDR thresholds is not clearly stated. While this appears to be a Bonferroni-type correction (p-value threshold divided by number of transcripts or metabolites tested), the thresholds do not reflect the actual number of tests performed (7883 transcripts times 453 metabolites for transcript-metabolite associations, 87 metabolites or 10435 transcripts times 28 complex phenotypes). The correct and more stringent thresholds certainly decrease the overlap between causal relationships and thus reduce the identifiable number of causal triplets. Furthermore, we believe that multiple testing has to be considered for correct interpretation of the power analysis. The study compares the power of a TWMR-only approach to the power of mediation-based MR by comparing "power(TP)" against "power(TM) * power(MP)" (p. 12). This comparison is useful in a hypothetical situation given data on a single transcript affecting a single phenotype, and with potential mediation via a single metabolite. However, in an actual empirical situation, the number of non-causal transcript-metabolite-phenotype triplets will exceed the number of non-causal transcript-phenotype associations due to the multiplication with the number of metabolites that have to be evaluated. This creates a tremendous burden of multiple testing, which will very likely outweigh the increase in power afforded by the mediation-based approach in the hypothetical "single transcript-metabolite-phenotype" situation described here. Thus, for explorative detection of causal transcript-phenotype relationships, the TWMR-only method might even outperform the mediation-based method described by the authors, simply because the former requires a smaller number of hypotheses to be tested compared to the latter. The presented simulation would only hold in cases where a single path of causality with a known potential mediator is to be tested.

We thank the reviewer for pointing out the multiple testing issue. Based on this comment, we have revised our approach by mainly implementing two major modifications to our approach.

First, we reduce the number of assessed metabolites to 242 compounds for which we were able to identify a Human Metabolome Database (HMDB) identifier through manual curation. This was triggered by the suggestion of reviewer #1 to facilitate the database/literature-based follow-up of our discoveries. The motivation is to only test metabolites that if found to be significantly associated would yield interpretable results, thereby reducing the number of tests to be performed. This modification is described in the revised manuscript:

Results: “Summary statistics for cis-eQTLs stem from the eQTLGen Consortium metaanalysis of 19,942 transcripts in 31,684 individuals [3], while summary statistics for mQTLs originate from a meta-analysis of 453 metabolites in 7,824 individuals from two independent European cohorts: TwinsUK (N = 6,056) and KORA (N = 1,768) [6]. After selecting SNPs included in both the eQTL and mQTL studies, our analysis was restricted to 7,884 transcripts with ≥ 3 instrumental variables (IVs) (see Methods, Supplemental Figure 1) and 242 metabolites with an identifier in The Human Metabolome Database (HMDB) [28] (see Methods, Supplemental Table 1).”

Methods: “mQTL data originate from Shin et al. [6], which used ultra-high performance liquid chromatography-tandem mass spectrometry (UPLC-MS/MS) to measure 486 whole blood metabolites in 7,824 European individuals. Association analyses were carried out on ~2.1 million SNPs and are available for 453 metabolites at the Metabolomics GWAS Server (http://metabolomics.helmholtz-muenchen.de/gwas/). Among these metabolites, 242 were manually annotated with Human Metabolome Database (HMDB) identifiers (Supplemental Table 1) and used in this study.”

Second, to account for all remaining tests, we now select significant causal effects based on FDR < 5% in all performed univariable MR analyses. With 5% FDR on both the transcript-to-metabolite and metabolite-to-phenotype effects, the FDR for triplets is slightly inflated to 9.75% (= 1-0.952), a consideration that we now explicitly describe. Note that selecting triplets based on transcript-tometabolite and metabolite-to-phenotype effects FDR < 2.5%, result in a FDR < 5% (1-0.9752) for the triplets. This more stringent threshold identifies 135 causal triplets, 39 of which would be missed by TWMR. Overall, Results and Supplemental Tables have been updated and now read as follow:

“Mapping the transcriptome onto the metabolome […] By testing each gene for association with the 242 metabolites, we detected 96 genes whose transcript levels causally impacted 75 metabolites, resulting in 133 unique transcriptmetabolite associations (FDR 5% considering all 1,907,690 instrumentable gene-metabolite pairs Supplemental Table 2) […].

Mapping the metabolome onto complex phenotypes […] Overall, 34 metabolites were associated with at least one phenotype (FDR 5% considering all 1,344 metabolite-phenotype pairs), resulting in 132 unique metabolitephenotype associations (Supplemental Table 4).

Mapping the transcriptome onto complex phenotypes […] In total, 5,140 transcripts associated with at least one phenotype (FDR 5% considering all 292,170 gene-phenotype pairs) resulting in 13,141 unique transcript-phenotype associations (Supplemental Table 5).

Mapping metabolome-mediated effects of the transcriptome onto complex phenotypes […] We combined the 133 transcript-metabolite (FDR ≤ 5%) and 132 metabolite-trait (FDR ≤ 5%) associations to pinpoint 216 transcript-metabolite-phenotype causal triplets (FDR = 1-0.952 = 9.75%) (Supplemental Table 6).”

In the simulations performed for the power analysis, we used a Bonferroni correction. We ran each simulation for 500 transcripts, measuring 80 metabolites at each run and performed TWMR and MWMR. The power of TWMR was calculated by counting how many times we obtain p-values ≤ 0.05/500. The power of the mediation analysis was calculated as 𝑝𝑜𝑤𝑒𝑟"$ ∗ 𝑝𝑜𝑤𝑒𝑟$#, where 𝑝𝑜𝑤𝑒𝑟"$ was calculated by counting how many times we obtain p-values ≤ 0.05/(500*80), and 𝑝𝑜𝑤𝑒𝑟$# was calculated by counting how many times we obtain p-values ≤ 0.05/80. In the revised manuscript, we additionally repeated each simulated scenario 10 times to increase robustness of results. This has been clarified in both the Methods and Results sections of the revised manuscript:

Methods: “Ranging 𝜌 and 𝜎 from -2 to 2 and from 0.1 and 10, respectively, we run each simulation for 500 transcripts measuring 80 metabolites at each run and performed TWMR and MWMR starting from above-described 𝛽7<"=, 𝛽4<"= and 𝛽>?,(. For each MR analysis we calculated the power to detect a significant association as well as the difference in power between TWMR and the mediation analyses (i.e., 𝑝𝑜𝑤𝑒𝑟"# − 𝑝𝑜𝑤𝑒𝑟"$ ∗ 𝑝𝑜𝑤𝑒𝑟$#). Each specific scenario was repeated 10 times and the average difference in power across simulation was plotted as a heatmap.”

Results: “To characterize the parameter regime where the power to detect indirect effects is larger than it is for total effects, we performed simulations using different settings for the mediated effect. In each scenario we evaluated 500 transcripts and 80 metabolites and varied two parameters characterizing the mediation: a. the proportion (𝜌) of direct (𝛼!) to total (𝛼"#) effect (i.e., effect not mediated by the metabolite) from -2 to 2 to cover the cases where direct and mediated effect have opposite directions (51 values); b. the ratio (𝜎) between the transcript-to-metabolite (𝛼"$) and the metabolite-to-phenotype (𝛼$#) effects, exploring the range from 0.1 to 10 (51 values).<br /> Transcripts were simulated with 6% heritability (i.e., median ℎ@ in the eQTLGen data) and a causal effect of 0.035 (i.e., ~65% of power in TWMR at a = 0.05) on a phenotype. Each scenario was simulated 10 times and results were averaged to assess the mean difference in power (see Methods).”

2) A second concern regards the interpretation of the results based on the empirical datasets. For the identified 206 transcript-metabolite-phenotype causal triplets, the authors show a comparison between TWMR-based total effect of transcripts on phenotypes and the calculated direct effect based on a multivariable MR (MVMR) test (Figure 2B), which corrects for the indirect effect mediated by the metabolite in the causal triplet. The comparison shows a strong correlation between direct and total effect. A thorough discussion of the potential reasons for deviation (in both negative and positive directions) from the identity line is missing.

Deviation from the identity line, as observed in Figure 2B, indicates that while there is a strong correlation between direct and total effect, it is not perfect, and part of the total effect is due to an indirect effect mediated by metabolites. This is explained and discussed in the Results and Discussion section:

Results: “Regressing direct effects (𝛼!) on total effects (𝛼"#) on (Figure 2A), we estimated that for our 216 mediated associations, 77% [95% CI: 70%-85%] of the transcript effect on the phenotype was direct and thus not mediated by the metabolites (Figure 2B).”

Discussion: “The observation that 77% of the transcript’s effect on the phenotype is not mediated by metabolites suggests that either true direct effects are frequent or that other unassessed metabolites or molecular layers (e.g., proteins, post-translational modifications, etc.) play a crucial role in such mediation. It is to note that in the presence of unmeasured mediators or measured mediators without genetic instruments, our mediation estimates are lower bounds of the total existing mediation. […] Thanks to the flexibility of the proposed framework, we expect that in the future and upon availability of ever larger and more diverse datasets, our method could be applied to estimate the relative contribution of currently unassessed mediators in translating genotypic cascades.”

Furthermore, no test of significance for potential cases of mediation is presented. Due to the issues of multiple testing discussed above, the significance of the inferred cases of mediation is drawn into question. The examples presented for causal triplets (involving the ANKH and SLC6A12 transcripts) feature transcripts with low total effects and a small ratio between direct and total effect, in line with the power analysis. However, in these examples, the total effects are also quite low. Its significance has to be tested with an appropriate statistical test, incorporating multiple testing correction.

Following the reviewer’s suggestion, we have modified our criteria to call significant associations to account for multiple testing (see extensive reply to major concern #1). With 5% FDR on both the transcript-to-metabolite and metabolite-to-phenotype effects, the FDR for triplets is slightly inflated to 9.75% (= 1-0.952). We mention this limitation in the revised manuscript:

“We combined the 133 transcript-metabolite (FDR ≤ 5%) and 132 metabolite-trait (FDR ≤ 5%) associations to pinpoint 216 transcript-metabolite-phenotype causal triplets (FDR = 1-0.952 = 9.75%) (Supplemental Table 6).”

All examples presented in the original manuscript remained significant. The fact that the total effect in these examples is low makes them particularly interesting as it highlights how our approach can detect biologically plausible associations between a transcript and a phenotype that only show mild evidence through TWMR but are strongly supported when accounting for metabolites that mediate the transcript-phenotype relation, showcasing situations in which our method can provide a true advantage over classical approaches such as TWMR. Such examples may emerge due to opposite signed direct and indirect effects, which cancel each other out when it comes to testing total effects. What is key that we do not claim the total and the mediated effects to be different (as we would have very limited power to do so), but simply point out that under certain settings we are better powered to detect mediated effects than total ones. In the ANKH example (more details below), the total ANKH-calcium effect is almost exactly the same as the product of the 𝛼,-.%→056157 and 𝛼056157→0120*34 effects, simply the latter ones are detectable, while the total effect is not.

In the revised manuscript the case for our selected examples is made even stronger thanks to an analysis proposed by Reviewer #1 that aimed at estimating the proportion of previously reported associations through automated literature review. For instance, while our literature review found previously reported evidence of the ANKH-calcium link and of the ANKH-citrate link, we did not identify any publication mentioning all 3 terms in combination in the abstract and/or title, illustrating how our approach can establish bridges between knowledge gaps. We revised the Results section describing the ANKH example accordingly:

“The 126 triplets that were not identified through TWMR due to power issues represent putative new causal relations. This is well illustrated by a proof-of concept example involving ANKH [MIM: 605145] and calcium levels, for which 48 publications were identified through automated literature review (Supplemental Table 6). While the TWMR effect of ANKH expression on calcium levels was not significant (𝛼,-.%→012034 = −0.02; 𝑃 = 0.03), we observed that ANKH expression decreased citrate levels (𝛼,-.%→056157 = −0.30; 𝑃 = 2.2 × 1089:), which itself increased serum calcium levels (𝛼056157→012034 = 0.07; 𝑃 = 6.5 × 108;9). Mutations in ANKH have been associated with several rare mineralization disorders [MIM: 123000, 118600] [32] due to the gene encoding a transmembrane protein that channels inorganic pyrophosphate to the extracellular matrix, where at low concentrations it inhibits mineralization [33]. Recently, a study proposed that ANKH instead exports ATP to the extracellular space (which is then rapidly converted to inorganic pyrophosphate), along with citrate [34]. Citrate has a high binding affinity for calcium and influences its bioavailability by complexing calcium-phosphate during extracellular matrix mineralization and releasing calcium during bone resorption [35]. Together, our data support the role of ANKH in calcium homeostasis through regulation of citrate levels, connecting previously established independent links into a causal triad.”

Furthermore, the analysis of the empirical data indicates that the ratio between direct and indirect effect of a transcript on a phenotype is in most cases close to identity, except for triplets with low total effects. This fact should be considered in the power analysis, which assigned the highest gain in power by the mediation analysis to cases of low direct to total effect ratio. The empirical data indicate that these cases might be rare or of minor relevance for the tested phenotypes.

As our previous power analyses did not fully reflect scenarios observed from empirical data, we extended the range of covered 𝜌 (i.e., the ratio between direct and total effect), so that it mimics more closely the observed range of 𝜌. In the revised manuscript, 𝜌 varies from -2 to 2, so that we also consider configurations where direct and total effects have opposite direction. To provide the readers with a rough idea how frequent the different parameter combinations occur in real data, we now provide another heatmap indicating the density of detected associations in those parameter regimes as Supplemental Figure 4.

This map can be brought in perspective of Figure 4A that illustrates the power of TWMR vs. mediation analysis over the same range of parameter settings.

It becomes apparent from Supplemental Figure 4 that in real data, 𝜎 is always larger than 1 and often exceeds 10. Note, however, that this heatmap must be interpreted with care, since the “detected” density will be low in regions where both methods have low power.

3) Related to the interpretation of causal links: horizontal pleiotropy needs to be considered. The authors report the identification of causal links between TMEM258, FADS1 and FADS2, arachidonic acid-derived lipids and complex phenotypes. However, they also mention the high degree of pleiotropy due to linkage disequilibrium at the underlying eQTL and mQTL region as well as the network of over 50 complex lipids known to be associated with the expression of the above transcripts. Thus, it seems possible that the levels of undetected lipid species may be more important for the phenotypic effect of variation in these transcripts and that the reported "mediators" are rather covariates. Such horizontal pleiotropy would violate a basic assumption of the MR approach. While we think that this does not invalidate the approach altogether, it does affect the interpretation of specific metabolites as mediators. This is aggravated by the fact that metabolic networks are more tightly interconnected than macromolecular interaction networks (assortative nature of metabolic networks) and that single point-measurements of metabolites may not be generally informative about the flux through a specific metabolic pathway.

This is a valid point and we discuss this limitation in the revised Discussion:

“It is to note that in the presence of unmeasured mediators or measured mediators without genetic instruments, our mediation estimates are lower bounds of the total existing mediation. In addition, unmeasured mediators sharing genetic instruments with the measured ones, can modify result interpretation as some of the observed mediators may simply be correlates of the true underlying mediators. While this is a limitation of all MR methods, metabolic networks may harbor particularly large number of genetically correlated metabolite species.”

Author Response

Reviewer #2 (Public Review):

This paper presents novel evidence for the successor representation in the hippocampus and V1 for temporally structured visual sequences. Participants learned sequences of 4 items shown in specific locations (A-B-C-D) on the screen. On a subset of trials, participants were only shown one of the four items, which enabled the authors to test whether the remaining three items were reactivated equivalently, or whether the upcoming items were activated in a temporally graded predictive fashion, consistent with the successor representation. The data suggest the latter interpretation, which was observed in both the hippocampus and V1.

The approach is well-motivated, and the hypotheses are laid out clearly. The manuscript is very clear and streamlined. The design adopted by the authors, which allowed them to disentangle spatial vs. temporal proximity, is clever and provides an interesting approach to the SR framework. The figures are also very clear and nicely designed. I just have a few comments which I hope the authors can address.

We thank the reviewer for the positive evaluation.

1) My main question is related to the difference between the analytic approach to V1 vs. hippocampal representations. In Fig. 3, the authors present evidence of a compelling gradation in V1 representations. However, the corresponding hippocampal results in Fig. 5 are collapsed across all predecessor vs. successor representations.

I initially thought that the same approach could not be taken in the hippocampus (-3/-2/-1 vs. 1/2/3) due to the coarser representation of space - is that the correct interpretation? However, on p. 9 the authors state that they successfully trained a hippocampal classifier based on spatial locations, so I was unsure why the same approach would not be possible. It would be helpful if the authors could add a sentence clearly explaining why the plots and analyses are not parallel across V1 and the hippocampus.

We appreciate the reviewer bringing up this point. The reviewer is correct, that in principle the same approach could be applied to both V1 and hippocampus. We have now added our motivation for collapsing the data for hippocampus and also appended the non-averaged hippocampus results as a Supplementary Figure. Below we copy our response to Reviewer #1 from above, who brought up a similar point.

Given the significant, but very low classification accuracy in within the localizer (accuracy = 15% 3.6%, mean ± s.d.; p = 0.002), we had previously decided to only report averaged location results for the hippocampus as the non-averaged predictions would be very noisy. To put the hippocampus classification accuracy into context, in V1 cross-validated accuracy within the localizer was 92% ± 12%, mean ± s.d.).

We now stressed this difference between V1 and hippocampus decoding in the Results section and motivate our reason for presenting averaged results:

"Within localizer decoding accuracy results confirmed that hippocampus has a coarse representation of the eight stimulus locations (Figure 5B) within the localizer (one-sample t-test; t(34) = 3.28, p = 0.002; cross-validated accuracy = 15%  3.6%, mean  s.d.; see Materials and Methods). Notably, compared to V1 (cf. Figure 2A), within localizer accuracy was relatively low and as a consequence tuning curves in hippocampus appeared less sharp (Figure 5C). In order to maximize sensitivity for the hippocampus, we averaged classification evidence across successor and predecessor locations. Non-averaged results can be found in Supplementary Figure 1A."

Further, we followed the reviewer’s suggestion and added a new supplementary Figure including the non-averaged results for hippocampus. The new Figure also includes the model comparison the reviewers had asked for. The new Supplementary Figure 1 is included here for convenience:

2) The analysis disentangling temporal vs. spatial proximity in the localizer data (Fig. 6) is interesting, particularly the persistent gradation in hippocampal responses vs. their absence in V1. However, could the same/similar temporal vs. spatial model not be applied in the full vs. partial sequences as well, as one of the alternative models shown in Fig. 4? The CO model in Fig. 4B assumes a flat reactivation of all other items in the sequence, but it might be that the two items closer in terms of Euclidean distance are represented differently than the far item. After reading the detailed methods, I wonder if this was not possible because the second presented item was always the furthest from the start (180 degrees), but it would be helpful if the authors could clarify this.

The reviewer is correct that the fact that the sequence order and spatial distance were not fully decorrelated (second presentation was always farthest away from starting dot, third and fourth dot always the same distance from start) prevents us from quantifying the interaction of the SR and CO model with a spatial model during the main task.

We added the following to the Method section to clarify this:

"Note that because within each dot sequence, temporal order and spatial distance were not perfectly decorrelated (e.g. the second sequence dot was always farthest apart from the starting dot), it is not possible to estimate the combined influence of the SR model and the spatial coactivation model on the observed BOLD activity."

Having said that, we believe that there is little concern that the reported reactivations of the main task are driven by the Euclidean distance in a meaningful way for two reasons:

(1) detailed analysis of the localizer data showed that there is no spatial spreading from one dot location to the other sequence locations (Figure 6). This is likely because the relevant dot locations were sufficiently spaced apart (at least 5.36 degrees of visual angle), whereas population receptive field sizes in V1 are well below 2 degrees (Dumoulin & Wandell, 2008). Given the lack of spreading during the localizer, where the dot was flashed for 13.5s, makes the presence of spreading during the main task, where the dot was flashed for only 100ms, equally unlikely.

(2) the presence of spatial spreading would actually obfuscate the reported SR-like pattern and could not have caused it. Specifically, because the second sequence dot was always farthest apart from the start, this is where one would assume the least amount of activity spread (greatest Euclidean distance). Sequence dots three and four should be more active given that they are both closer to the starting point in terms of Euclidean distance. Our reported results are the opposite of that pattern, ruling out the possibility that these were caused by spatial spreading.

3) As the authors state on p. 12, the present study did not require any long-term prospective planning. However, the participants' task during the full sequences was closely linked to their predictions about the temporal structure of the four stimuli. It would be useful to see whether the participants who were more closely 'locked' to the sequence and accurate at this temporal detection task also showed stronger SR representations (as these rely on temporal distance).

This would also provide a useful test of the timescale at which successor representations are behaviorally relevant. In several prior studies, the timescales were quite long, so it would be important to test how strongly SR representations at these timescales relate to behavior.

We thank the reviewer for this suggestion. In order to relate SR representations to behavior, we first calculated individual BOLD differences for successor vs predecessor locations to get an estimate for how much participant’s predictions were skewed toward future locations. One might argue, that participants with stronger predictions toward future locations would perform better at the behavioral task. We then correlated these values with behavioral accuracy across subjects. No significant correlation was found (r = 0.05; p = 0.769). The lack of significant correlation might not be surprising, given that our design is likely underpowered for such a between-subject correlation analysis. Additionally, there was no behavioral response in the prediction trials, that could be directly related to participants’ BOLD activity. Instead the behavioral response is taken from the full sequence trials.

These new results were added to the results section:

"One might argue that participants with stronger predictions toward future locations would perform better at the behavioral detection task. However, no such correlation between individual V1 BOLD activity and task accuracy was found in an across subject correlation analysis (see Materials and Methods, spearman r = 0.05; p = 0.769)."

And described in the methods:

"Correlation with behavior. In order to relate SR representations to behavior, we first calculated individual V1 BOLD differences for all successor vs all predecessor locations to get an estimate for how much participant’s predictions were skewed toward future locations. We then correlated these values with behavioral accuracy across subjects using spearman correlation."

Author Response

Reviewer #2 (Public Review):

In the manuscript, Mijnheer et al mainly exploited CyTOF Helios mass cytometer and TCRβ repertoire sequencing to investigate the T cell composition and distribution in peripheral blood and synovial fluid, and further explored the temporal and spatial dynamics of regulatory T cells (Tregs) and non-Tregs in the inflamed joints of Juvenile Idiopathic Arthritis (JIA) patients. Their results indicate that the activated effector T cells and hyper-expanded Treg TCRβ clones found at the inflamed joints are highly persistent in the circulation, and the dominant of high degree of sequence similarity of Treg clones could serve as the novel therapeutic targets for the JIA treatment. Overall, the research design is appropriate, and the methods are adequately described in the study. However, several issues are required to be addressed.

(1) The criteria for the JIA patient's recruitment should be clearly presented in the method section. For example, what is the specific included criteria and excluded criteria? Or did the patients take medicines for the treatment during the study?

A total of 9 JIA patients were included in this study. Of these, n=2 were diagnosed with extended oligo JIA, n=2 with rheumatoid factor negative poly-articular JIA, and n=5 with oligo JIA, according to the revised criteria for JIA. The average age at the time of inclusion was 13,1 years (range 3,2 – 18,1 years) with a disease duration of 7,3 years (range 0.4 – 14.2 years). Due to limited sample availability, we did not have strict inclusion or exclusion criteria for JIA patient recruitment. For CyTOF analysis, patients were selected based on the criteria that the left and right knee joints should both be affected at the time of inclusion. For sequential TCR sequencing analysis, we included patients with a refractory disease course. At the time of first inclusion, patients were treated with non-steroidal anti-inflammatory drugs (NSAIDs) or methotrexate, but no biologicals. For the refractory time point samples, patients were treated with disease modifying anti-rheumatic drug (DMARDs) (leflunomide) and/or biologicals (Humira) after first sample inclusion due to the refractory nature of their disease.

We have now updated the methods section (lines 455-463) of the revised manuscript with more information on patient recruitment, and included information on diagnosis, sex, age, disease duration and medication for every patient in Supplementary File 1.

(2) As for the correlation analysis of the entire spectrum of node frequencies, the SFMCs and PBMCs isolated from 3 patients were conducted in the study. The sample size is too limited to obtain robust results and to make a convincing conclusion from the correlation analysis. And it is shown that a total of 9 JIA patients have been involved in the study. Could the author clarify it?

In order to strengthen our observations, we now included single-cell transcriptomics data obtained from Zhang, et al. (https://doi.org/10.1038/s41590-019-0378-1). In this data, we identified a cluster of CD4+FOXP3+ Tregs (new Figure 2-figure supplement 2A and 3B) that showed increased frequency in RA patients (new Figure 2-figure supplement 2C), consistent with the high frequency of Tregs that we observed in our JIA SFMC samples. Additionally, the expression of markers of chronic TCR activation (PDCD1 (PD1), CTLA4 and ICOS), and cytokines (TNF, IFNG and GZMB) were significantly increased in RA compared to OA, in line with what we observed in JIA SFMC (new Figure 2-figure supplement 2D). These results demonstrate that, although the number of JIA patients included in our study is low, obtained results are robustly reproducible in an independent, comparable dataset.

We do agree with the reviewer that the low number of patients included in our study warrants further validation. Therefore, we have now added the following line in the discussion to highlight this (lines 369-371): “Further validation of our observations in larger cohorts of JIA patients should help to substantiate these results and aid the identification of pathogenic Treg populations across patients.”.

Regarding the number of patients included in our studies, we have now included Supplemental File 1, which clarifies which JIA patients have been used for each analysis in our study.

(3) The results of the study indicate that the hyper-expanded T cell clones are shared between left and right knee joints. Since JIA may affect one or more joints, did the author check other joints to see if the same expanded T cell clones infiltrate multiple joints, such as hand or wrist?

Indeed, it would be interesting to see whether hyper-expanded clones are shared between multiple inflamed joints other than knees. However, samples from other locations are very difficult to obtain and very little synovial fluid can be extracted from joints such as hands and wrists. Therefore, the number of cells obtained from these joints would be too limited to perform mass cytometry or TCR sequencing. Thus, we chose to focus on synovial fluid from knee joints in our studies. Moreover, for oligoarticular JIA patients, only the large joints are affected (of which the knees are most typical), so for these patients it would not be possible to include other joints.

(4) For Fig.2B, the Treg CD25+FOXP3+ population was significantly enriched in synovial fluid (SF). Is it from the left knee joints or the right knee joints?

Figure 2B shows data from both knee joints. We have now clarified this in the figure legend by adding “For SFMCs, data from the right and left knee joints for all patients is shown” (lines 179-180).

And in the context of Line 144-148, it indicated the SF, however, the title of axis in Fig.2B indicated Synovial Fluid Mononuclear Cells (SFMCs). Please keep consistent.

We thank the reviewer for bringing this to our attention. We have critically revised the manuscript and made the use of SF versus SFMCs more consistent.

(5) For the longitudinal sampling timelines of JIA patients shown in Supplementary Fig.3, the interval of PB and SF sample collection is not consistent. And only 1 patient completed 4 visits and the sample collection. It is hard to make any conclusion from 1 patient.

In our study, we had longitudinal samples available for 5 JIA patients for which we performed TCR sequencing of Tregs from SFMCs from different joints (right or left) at least two time points. In the manuscript we mainly focused on patient 1, as for this patient the largest amount of data was available. However, for all other longitudinal patient samples included, we also show that dominant clones persist over time (Figure 4A and 5A). To further highlight that our observations are not just applicable to one patient, but consistent for all patients included, we now included detailed analysis for all patients in Figure 4-figure supplement 3 and Figure 5-figure supplement 1. This analysis shows that frequencies of shared TCRβs are consistent over time in all patients.

Author Response

Reviewer #1 (Public Review):

Detecting and quantifying balancing selection is a notoriously difficult challenge. Because the distribution of times to fixation or removal of strictly neutral variants has a long tail, it can be hard to exclude the null hypothesis of neutrality when testing for balancing selection that was not established so long ago that trans-specific variants can be observed. As Aqil et al. point out, most efforts to detect balancing selection in the human genome have been focused on single nucleotide variants. The authors seek to characterize the amount of balancing selection specific for polymorphic deletions. The authors justify their focus based on the fact that deletions are more likely to have functional consequences than single nucleotide variants, making it more likely that if they have remained for many generations, this could be a signature of balancing selection. That said, multiple aspects of the analysis deserve more attention.

I have two broad concerns about the manuscript that the authors need to address. First, the authors use neutral simulations to exclude that neutrality alone can explain the amount of allele sharing observed between African modern humans and the archaic genomes. My concern is that human demography models, including the one from Gravel et al. (2011) used by the author are always simplifications of the complex demographic events that shaped human populations during evolution. In the case of the specific model used by the authors, African populations were inferred by the Gravel et al. model to have a constant population size for the past ~150,000 years (parameters Taf and Naf in the original model). This is an unrealistic assumption of this model. In brief, I am wondering how much the claim of the authors that neutrality alone cannot explain patterns of allele sharing is potentially based on mis-specifications of the neutral demography model. For example, the more fine scale fluctuations of effective population sizes in Africa inferred by author L. Speidel in 2019 Nature (Figure 3) paint a different picture than the Gravel et al. model. The authors need to run extensive testing of the robustness of their conclusions to changes in the neutral demographic model used. What if the average ancestral population size was closer to 20,000? What if it was closer to 50,000 and frequency fluctuations every generation were smaller? Given how uncertain past population sizes really were and the current uncertainties about demographic reconstruction in particular relative to linked selection, the authors need to explore a range of past population size beyond the idiosyncrasies of a specific model.

These are great suggestions. Based on them, we now conducted 37 additional simulations with different sets of parameters, including adding the Speidel et al. model to the mix (the new Figure 1C). As discussed above (please refer to our response to the general reviews) and in the Results section, realistic neutral scenarios cannot explain the excess allele sharing.

My second broad concern is that it is difficult to evaluate how novel the findings really are. It is true that the authors focus on deletions while pasts scans for balancing selection in the human genome focused on SNVs. But it could be the case that a substantial number of the deletions identified here as under balancing selection could have previously been identified as such loci through linked SNVs by the scans cited by the authors. The authors need to provide quantification of how many of their deletions are truly novel balancing selection loci as opposed to balancing selection loci already identified through linked SNVs.

The reviewer is right. We now compared our results with previous genome-wide studies, which have been notoriously inconsistent with each other. We found that virtually all of our candidates are novel, as described in our response to the general reviews and our Results section.

The novelty of the balanced deletions will also be better established by providing a more quantitative and less anecdotal functional analysis. It is true that the deletions include immune loci, but are they statistically enriched for immune loci as annotated for example by Gene Ontology, in a way that shows that their distribution across the genome is not random but indeed driven by selection enriching them at loci with specific functions? In addition, do the pie charts in Figure 5E, represent a statistically significant deviation from left to right or not?

We appreciate the reviewers’ suggestions, which led us to conduct a series of very fruitful analyses. As discussed above, we now found that ancient deletions are significantly more likely to have GWAS traits and be exonic (Figure 5B) and significantly more likely to affect immunity, blood, and metabolism-related traits (Figure 5C). Moreover, we found that ancient deletions are depleted for smaller size categories but show significant enrichment for the sizes 95th percentile and above (Figure 7A). We now discussed these findings in the Results section.

Reviewer #2 (Public Review):

The authors assess evidence for balancing selection by looking at old polymorphisms where the derived allele is shared by descent with archaic humans, meaning the polymorphism must predate this split. Using simulations and several features of these old polymorphisms, they evaluate whether and what signatures of balancing selection are enriched in these polymorphisms. This is a well-explained and thorough analysis, and a clever way to approach a difficult question, yet the analysis remains fairly descriptive and the claims that can be made are not strong. For instance, the title of the paper does not state a particular finding of balancing selection, and several claims are "may" such as "A significant portion of ancient polymorphisms may have evolved under medium-term balancing selection" and "These results suggest that at least 27% of common functional deletion polymorphisms may have been evolving under balancing selection".

We thank the reviewer for their insights. We agree that balancing selection is a difficult to elucidate definitively. However, in our revisions, we have conducted several additional analyses based on reviewers’ suggestions as discussed under individual comments. We believe that these analyses strengthen our claims.

First, using simulations, they show there are more such ancient nonsynonymous and (indirectly) deletion variants than expected under a simple neutral model. The enrichment is nominal when compared only with Denisovan sharing, which could be explained due to some superarchaic ancestry in Denisovans (though not clear if that holds up quantitatively). The classification of the shared polymorphisms as recurrent, recently introgressed, or ancient shared by descent could be more carefully tested. In particular, I'm concerned about the possible inclusion of recurrent mutations among the ancient set. Although the age trend is consistent, it does not indicate how much misclassification there might still be. For example, there are "ancient" deletions that have inferred ages more recent than the human-archaic split (shown in Fig. 3).

We agree that recurrent mutations are crucial to discriminate from the ancient ones in our analysis. We have now conducted additional analysis of allele frequency and CG content to further test potential recurrent mutations in our datasets as described in our response to general reviews. We described these in our Results section and Figure S1. In addition, we actually conducted even more stringent filtering requiring perfect LD and found that this increased stringency did not affect our results substantially. Thus, we believe that our pipeline identifies ancient deletions very conservatively and likely harbors a considerable number of false negatives, where ancient deletions are categorized as recurrent.

The reviewer’s observation that some ancient deletions have recent dates is indeed interesting. The dating of individual alleles assumes neutrality and broadly depends on haplotype length and allele frequency. We believe that given the potential soft sweeps acting on these deletions, it is possible that the dates may be biased in some cases. For example, if there is a recent sweep on an ancient deletion, this may lead to longer haplotype lengths and, thus, a more recent date for these alleles. Therefore, the ancient derived alleles (those that are shared with archaic hominins) which happen to have recent allele dates may be of particular interest for future scrutiny. We now discuss this particular issue further in the Results section as follows:

“Counterintuitively, some “ancient” deletions have very recent dates. This may be due to instances of recent soft sweeps involving some deletions leading to an increased length of the associated haplotype and an artificial decrease in age. Secondly, some ancient deletions may have low frequencies, which too creates a downward bias in age. Lastly, this may be due to rare instances of miscategorization of non-ancient deletions as ancient.”

For the rest of the paper, the authors then focus on the deletion variants, showing that these ancient deletions show an elevated signature of balancing selection (stdbeta2) but do not show less variance in allele frequency over time as would be expected under an overdominance model. They infer the mechanism to be spatial or temporal variation in selection or negative frequency-dependent selection by process of elimination. They identify the subset of ancient deletion polymorphisms that overlap exons and are associated with phenotypes, finding a high proportion of ancient deletions that fall in both these categories. The identification of this set of potentially causal deletions that may be under balancing selection is a set that is of interest to the wider community for follow up (though several have already been the subject of study and individual publications from this lab). Overall, this is a useful combination of simulation work and assessment of an intriguing set of old deletion polymorphisms. Put together, the analysis does support evidence of balancing selection on some of them, but the extent is still not clear.

We thank the reviewer. To further determine the extent of balancing selection acting on these ancient deletions, we conducted several enrichment analyses described above (please refer to our response to the general reviews) and in the paper. Briefly, we now added Figures 5B, 5C and 7A to describe these new analyses.

Author Response

Reviewer #1 (Public Review):

This study demonstrates the role of the circadian clock in spatiotemporal regulation of floral development. The authors nicely illustrated floral development patterns in domesticated sunflower. In particular, during anthesis, discrete developmental zones, namely pseudowhorls, are established, and hundreds of florets simultaneously undergo maturation in each psudowhorl in a circadian-dependent manner. Consistently, the flower development follows key features of the circadian clock, such as temperature compensation and gating of plant response to environmental stimuli. Evolutionary advantages of this regulation will add more merit to this study.

We thank the reviewer for this suggestion. We have performed new experiments (Figures 7 and 7-S1) that demonstrate that delays in anthesis relative to dawn and disruption of pseudowhorl formation both negatively impact pollinator visits to flowers. These findings suggest that circadian and light regulation of floral anthesis may have significant impacts on male reproductive fitness.

Reviewer #2 (Public Review):

Little is known about how the circadian clock regulates the timing of anthesis. This manuscript shows that the circadian clock regulates the diurnal rhythms in floral development of the sunflower. The authors have developed a new method to characterize the timing of floral development under normal conditions as well as constant dark and light conditions. The results from the treatment of darkness during the subjective night and day suggest that the circadian clock regulates the growth of ovary, stamen, and style differently.

All clock papers claim that the circadian clock regulates the fitness of organisms, however, it is hard to evaluate how the circadian clock affects the fitness of organisms. The timing of pollen release and stigma maturity is directly related to plant fitness. That's why the authors suggest that the circadian clock in sunflowers increases plant fitness by regulating the timing of anthesis.

Although the authors manipulated the light and temperature to examine the role of the circadian clock in floral development, the weakness of this manuscript is that there is no molecular evidence to show how the clock regulates floral development.

We acknowledge that this study does not demonstrate the molecular mechanisms by which the circadian clock and environmental sensing pathways regulate floral anthesis in sunflower. However, we feel that our demonstration that the circadian clock is involved in the generation of spatial patterns of development on the sunflower inflorescence disk is in itself novel and significant.

Reviewer #3 (Public Review):

The flowering heads of species in the Asteracaeae comprise large number of flowers, and this phenotype is thought to contribute to their reproductive success. The Harmer lab has developed sunflower as an experimental model to investigate the contribution of circadian regulation to the processes of reproduction in the Asteraceae, and this paper presents a new addition to this line of research.

The novelty of the article is that it resolves unanswered questions around the processes that underlie coordinated flowering within the disc structure of the floral capitulum. The authors demonstrate a role for circadian clock in the temporal structuring of this process. They identify a free running rhythm in constant darkness of floral anthesis, and this rhythm has several key characteristics of circadian rhythms. The data collected also indicate that the circadian clock might gate the response of anthesis to darkness.

I like the presentation of an external coincidence model for the interaction of light and circadian cues in the floral developmental program of the capitulum. However, I wonder whether this is the only potential explanation. The data in Fig. 4C look like classical entrainment responses. Are the authors sure that they are not just seeing an entrainment process within the capitulum, combined with a masking effect of continuous light upon the rhythmic phenotype? I encourage the authors to retain speculation about the coincidence model within the discussion- it's so important for future work- but perhaps consider alternative interpretations of the data also.

We thank the reviewer for their positive comments and overall enthusiasm for the study. We agree that it is entirely plausible that continuous light masks circadian clock-controlled rhythms in floral organ development; in our view, this is a restatement of the external coincidence model. We argue that in developing sunflowers, a circadian clock-regulated process controls elongation of floret organs. Normal development depends upon a dark period of at least 4.5 hours occurring during the subjective night. In constant light conditions, or early in re-entrainment when the dark period occurs during the subjective day, normal development is inhibited. This model is analogous to the photoperiodic control of flowering time in short-day plants, in which light perceived during the subjective night inhibits the floral transition.

Author Response

Reviewer #1 (Public Review):

Tafenoquine is an important 8-aminoquinoline antimalarial, mostly aimed at the management of Plasmodium vivax malaria. Through the retrospective analysis of several previously performed efficacy trials, the authors aimed to better understand the drugs mechanism of action, while exploring the possibility of improved efficacy through dose increment.

Strengths: robust analysis approaches unlocked three main messages with the potential of improving the clinical practice:

i. P. vivax recurrency is positively associated with tafenoquine terminal half-life and D7 methemoglobin levels.

ii. The methemoglobin levels support the current view that tafenoquine, acts through its metabolites, similar to what is believed for primaquine.

ii. Most importantly, the therapeutic window of tafenoquine is wider than previously considered, allowing the suggestion of a significant increase in dosing, from 300 mg to 450 mg, leading to significantly increased efficacy.

Weaknesses: being a retrospective analysis, the work is limited to the available data. In particular, and as referred by the authors, no drug levels are reported. Additionally, there are some aspects that in my view need more detailed analysis and discussion, in particular, what seems to be a lack of exploration as to the importance (or lack of it) of the patient CYP2D6 status in Tafenoquine T1/2, methemoglobin levels, and overall efficacy. These mild weaknesses do not change the overall conclusions of the study.

We thank the reviewer for their positive comments.

The analysis estimates the parameters of the PK model from 4499 measured drug concentrations measured for 718 individuals between days 0 and 180. The active metabolites of tafenoquine are unknown and thus could not be quantified.

Whilst the study is retrospective it includes 77% (651/847) of all patients enrolled in published P. vivax treatment trials of tafenoquine.

We respond to the relationship between CYP2D6 polymorphisms and the other outcomes in our response to Reviewer #1, Comment 2.

Reviewer #3 (Public Review):

By assembling the vast majority of global tafenoquine pharmacology data from clinical treatment studies that led to the 8-aminoquinoline's registration in 2018, the authors of this manuscript have convincingly made their argument that the currently recommended treatment dosage of 300mg (in combination with chloroquine) is too low and needs to be increased by at least 50%. Access to the multiple data sets is thorough, the modelling reasonable and the conclusion reached is sound.

How did we get here (again) under-dosing malaria patients with a class of drugs we have been working on for a century? Speaking as someone who was associated with tafenoquine development over two decades, it seems that worry about adverse events, specifically hemolysis in G6PD deficient persons, overcame the operational requirement to give enough drugs in a single dose regimen. However, tafenoquine is very safe in G6PD normal persons who by definition were the ones entered into the clinical treatment trials. Risk-benefit judgments cannot always be weighted towards "safety" especially when the real concern was that a single severe adverse event would derail the entire development program. Real-world effectiveness matters and should now result in the studies the authors state are needed to certify the higher dose regimen.

1) The schizophrenic nature of tafenoquine development needs to be mentioned. This manuscript discusses malaria treatment and includes nearly all the relevant data, but extensive work was also done to support the chemoprophylaxis indication largely sponsored by the US Army. These prophylaxis efforts were often separate from the parallel efforts on treatment indication to the loss of both groups who were ostensibly working on the same drug. 450mg tafenoquine is not a large dose; 600mg (over 3 days) is routinely given at the beginning of malaria chemoprophylaxis. Up to twice that amount was given in phase 2 studies done in Kenya in 1998 which resulted in the only described severe hemolytic reaction when one G6PD deficient heterozygote woman was given 1200mg over 3 days due to incorrect recording of her G6PD status. It is not easy to hemolyze even G6PD-deficient erythrocytes due to the slow metabolism of tafenoquine. Nearly all clinical trials of both primaquine and tafenoquine have experienced similar hemolytic events when there were errors in the determination of G6PD status. This does not mean that all 8-aminoquinolines are dangerous drugs, only that a known genetic polymorphism needs to be accounted for when treating vivax malaria.

It is notable that much larger doses of tafenoquine have been evaluated previously and these have been well tolerated in individuals with G6PD activity >30% (previous studies used semi-quantitative tests). We have added a review of all patients with P. vivax malaria who have been studied in treatment trials. A total of 847 were enrolled in all studies and our series contains individual patient data on 651 (77%) of these patients.

We have added the following to the Discussion on lines 277-283:

“Much larger doses have been studied in treatment and prophylaxis trials (up to 2100mg given over one week, Walsh et al., 1999, see Supplementary Appendix). The only report of a severe haemolytic reaction occurred in a female patient heterozygous for G6PD deficiency (A- variant) and received a total dose of 1200mg tafenoquine over 3 days (Shanks et al., 2001). In the same study, a homozygous female (A- variant) who was also given 1200mg tafenoquine over 3 days had an estimated 3g/dL drop in haemoglobin, but remained asymptomatic.”

2) The authors point out the utility of 7-day methemoglobin concentrations in predicted drug success/failure in the prevention of subsequent relapses. This is important and stresses the requirement of drug metabolism to a redox-active intermediate as being a common property of all 8-aminoquinolines. Tafenoquine and primaquine are similar but not identical and the slow metabolism of tafenoquine to its redox-active intermediates explains its main advantage of being capable of supporting a single-dose cure. The main reason this was not appreciated much earlier is we were looking in the wrong place. Metabolic end-products (5,6 orthoquinones) are in very low concentrations after single-dose tafenoquine in the blood, but being water-soluble they are easily located in the urine. Such urine metabolites indicative of redox action are very likely to be complementary to methemoglobin measurements which mark the redox effect on the erythrocyte. Despite earlier simplifying assumptions made during tafenoquine development (no significant metabolites exist), metabolism to redox-active intermediates must be embraced as the explanation of drug efficacy and not a cause of undesirable adverse events.

Another dark cloud over tafenoquine mentioned by the authors was the very disappointing results of the INSPECTOR trial in Indonesia whose full results are yet to be published. The failure of P vivax relapse prevention using 300mg tafenoquine with dihydroartemisinin-piperaquine in Indonesian soldiers was largely ascribed to under-dosing. Although this may have been partially true, another aspect indicated in figure 15 of the appendix is the nature of the partner drug. Artemisinin combinations with tafenoquine do not produce the same amount of methaemoglobin (indicative of redox metabolism) as when combined with the registered partner drug chloroquine. We do not understand tafenoquine metabolism, but it is increasingly clear that what drug is combined with tafenoquine makes a very substantial difference. Despite the great operational desire to use artemisinin combination therapy for all malaria treatment regimens, this may not be possible with tafenoquine. Chloroquine likely is driving tafenoquine metabolism as it has no real effect on latent hypnozoites in the liver by itself. Increased dose studies with tafenoquine need to be done with chloroquine, not artemisinin.

We are aware that this is an area of intense interest and that ex vivo data were presented at the recent ASTMH conference in Seattle suggestive of a drug-drug interaction between artemisinisin and tafenoquine. However, there are as yet insufficient in-vivo data to conclude with tafenoquine reducing the methaemoglobin concentration indicative of reducing redox metabolism compared to chloroquine and tafenoquine. In addition these data as yet unpublished.

Author Response

Reviewer #1 (Public Review):

This paper is a continuation of other research by this group and represents another step back in time for peptide preservation in eggshells. It is exciting to see Miocene age peptides and that they overlap so completely with both extant ostrich struthiocalcin as well as the previously described Pliocene peptides. The biggest weakness is the lack of tables showing both the de novo peptides as well as those detected by database searching.

We thank the Reviewer for their positive assessment of our work. We now provide a table with peptides identified by database searching as well as the annotated tandem mass spectra for the peptides.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Germanos et al present preclinical evidence of a dynamic interplay between tumor microenvironmental elements underlying prostate cancer initiation, progression, and emerging therapeutic resistance in the transgenic mouse model. The authors identify an intermediate luminal cell population trans-differentiating from a hypo-proliferative basal cell subset, meanwhile, hyper-proliferative basal cells replenish a non-differentiating basal subpopulation. The meticulous methodologic approach identifies candidate cellular interactions in fibroblasts, MDSCs, and immune cell populations associated with PTEN loss. The generalization of these findings to human data sets is of particular interest and recommended for future studies on this topic. Mechanistic studies with multi-cellular co-culture models are needed to extend and validate the findings in this report.

We thank the reviewer for finding our research “meticulous” in its approach. We agree that validating our findings in human contexts is a vital next step and have added new orthogonal datasets in the revised manuscript (Figure 4D-E). We also agree that complex molecular studies will be needed to fully evaluate our cell-cell interaction hypotheses. To this end, we have elaborated on appropriate follow-up studies in the discussion (Lines 625-628, 642-643, 657-659, 675-677).

Strengths and Weaknesses:

The study focuses on a clinically highly relevant and timely topic. The strength of this manuscript is the meticulous description of the Methods and model development and the integration of state-of-the-art orthogonal data sets. However, the number of data points across the experiments (n = 2 or 3) with considerable variability in the Ptenfl/fl group limits the interpretation of findings. Additionally, further experiments are needed to validate these observations in human prostate cancer and establish the potential translational relevance of these findings.

We are ecstatic that the reviewer finds our study “clinically highly relevant.” We agree that the low sample size is a potential limitation but believe that our overall results are robust and enable concrete conclusions for both epithelial and immune cell populations. This is in part because we validated our findings in orthogonal human datasets (Figure 4A-C, Figure 5H) in the original manuscript. However, to add rigor to our study, we have conducted new scRNAseq analysis showing that our findings correlate well with both human patient data (Figure 4D-E) and orthogonal mouse models (Figure 4F-G). Furthermore, we conducted additional scRNAseq on castrated WT murine prostate to demonstrate how castration plays an important role in translational heterogeneity in intermediate cells (Figure 4H, Figure 3 – figure supplement 1G).

As such, the report is fairly descriptive, and expanding the discussion on the mechanistic studies needed to identify which of these interactions drives aggressive prostate cancer would improve this report.

We agree with the reviewer that additional discussion of follow-up studies is necessary. As such, we have updated the discussion to highlight the molecular studies needed to fully characterize the cellular phenotypes described in this manuscript (Lines 625-628, 642-643, 657-659, 675-677).

Reviewer #2 (Public Review):

This work provides a thorough characterization of tumor cell and microenvironment dynamics in a castrate Pten null prostate cancer model and details the strength of cellular interactions using single-cell RNA sequencing. The search for a preexisting castrate-resistant prostate progenitor has been upended in recent years with the discovery that prostate luminal cells adapt to low androgen environments by undergoing lineage plasticity rather than an expansion of proximal progenitors. This paper provides indirect evidence that basal epithelia give rise to 'intermediate' epithelia through increased translation in intact and castrate Pten null mice cells, which is validated in a Pten null, 4ebp1 mutant mouse model.

Strengths:

The single-cell data are robust and expertly presented in the figures. The methods are largely appropriate and the delineation of experimental protocols is straightforward. The analysis is comprehensive and well described in relation to biological questions of interest to the community. The validation of the effect of translation on prostate epithelial viability in relation to initial findings advances our understanding of how cells survive in low androgen environments. The addition of a public portal for the data is highly useful.

We thank the reviewer for evaluating our work as “robust and expertly presented,” “comprehensive,” and “highly useful.”

In response to the reviewer’s in-depth comments, we have revised our nomenclature of WT epithelial cell subtypes to specifically distinguish between Krt4+/Tacstd2+ urethral, prostatic, and cancer-derived cells (Lines 163-185). We now find urethral and luminal progenitor groups in WT intact mice, which are distinct from “intermediate” cells arising from Pten loss (Figure 1 – figure supplement 1D-F). We have accordingly revised our interpretation of the potential origins of these intermediate cells in cancer (Lines 256-275).

Weaknesses:

The PB-Cre4 promoter seems to be promiscuously inactivating Pten in basal, intermediate, and luminal cells, which is problematic as this confounds the ability to differentiate between cells that are undergoing lineage plasticity vs. expansion of a pre-existing progenitor cell type. Much recent evidence points to lineage plasticity of prostate luminal tumor cells under androgen deprivation rather than survival and expansion of a pre-existing castrate-resistant basal or intermediate cell type. Accordingly, the observation that basal epithelia may transdifferentiate to intermediate epithelia or that a pre-existing intermediate luminal cell state is expanded under castration may be artifacts of the model without reproduction in human prostate cancer. The use of trajectory analysis of single-cell data to demonstrate basal or intermediate cell lineage transdifferentiation is a weaker type of evidence than the lineage tracing of individual cell types provided by other groups, which argue against transdifferentiation and for lineage plasticity.

This is a very thoughtful and nuanced comment. We agree that the PB-Cre4 promoter is promiscuously inactivating Pten in basal, luminal progenitor cells, and luminal cells which does confound the ability to differentiate between cells that are undergoing lineage plasticity versus expansion of pre-exisiting progenitor cell types. As such, we now expand our results section to include non-basal routes to the expansion of the Pten intermediate cell population (Lines 261-275). Furthermore, we also comprehensively discuss the limitations of our models in the discussion section highlighting the need to validate our findings using lineage tracing or newer techniques such as DNA Typewriter (Lines 616-628) (Choi et al., Nature 2022).

Currently it is not possible to conduct lineage tracing within the human prostate making it impossible to determine if basal epithelia may transdifferentiate to intermediate epithelia or if a pre-existing intermediate luminal cell state is expanded under castration. However, we do present new human scRNAseq data that the intermediate cell state, as reflected by the 5-gene castration signature, is enriched specifically in metastatic, but not localized prostate cancer (Figure 4D-E). Furthermore, we show that this gene signature is also relevant in a completely different progression model of murine prostate cancer (Figure 4F-G). Thus, while not perfect, our model does have potential human relevance despite the limitations which we address in the manuscript (Lines 261-275, 616-628).

Author Response

Reviewer #1 (Public Review):

Kang et al. have performed whole exome sequencing of gall bladder carcinomas and associated metastases, including analysis of rapid autopsy specimens in selected cases. They have also attempted to delineate patterns of clonal and subclonal evolution across this cohort. In cases where BilIN was identified, the authors show that subclones within these precursor lesions can expand and diversify to populate the primary tumor and metastatic sites. They also demonstrate subclonal variation and branching evolution across metastatic sites within the same patient, with the suggestion that multiple subclonal populations may metastasize together to seed different sites. Lastly, they highlight ERBB2 amplification as a recurrent event observed in gall bladder carcinomas.

While these data add to the literature and start to examine important questions related to clonal evolution in a relatively rare malignancy, the authors' findings are very descriptive and it is hard to draw many generalizable conclusions from their data. In addition, the presentation of their figures is somewhat confusing and difficult to interpret. For example, they do not separate their clonal analyses by disease site and by time in a readily interpretable manner, as in some instances of Figure 2 and Figure 3 the clone maps are from different sites collected at the same time point, while others show some samples at different time points. Depicting these hierarchies in a more organized and clearly understandable manner would help readers more easily interpret the authors' findings. In addition, the clinical implications of these clonal hierarchies and their heterogeneity are unclear, as the authors do not relate the observed evolution to intervening therapies and may not be powered to do so with this dataset.

Thank you for the constructive and valuable comments about 1) figures and 2) clinical implications.

1) We agree with your opinion that Figures 2 and 3 are confusing. Reflecting on your comment, Figures 2 and 3 have been modified. Now, the time point at which the tissue was obtained and the anatomical location of the tissue are readily visible in the redesigned figures.

2) From a clinical point of view, we believe that our study highlights the importance of precise genomic analysis of multi-regional and longitudinal samples in individual cancer patients. In the current oncology clinics, cancer panel data of patients are being used to identify druggable mutations usually with a single tumor sample. However, we found that only a part of the mutations was clonal while a substantial proportion was subclonal, which is usually not an effective druggable target. For example, in the GB-S2 patient, after sequencing with GB tissue, ERBB2 targeting treatment would have been performed if a specific clinical trial is available because ERBB2 p.V777L is pathogenic. However, our clonal evolution analysis suggests that ERBB2 targeting strategy may not be effective in subclones without the ERBB2 p.V777L mutation, especially from regional metastasis. We have added the description for this part to the Discussion section (Page 13, Line 12-15).

Additional areas that would require clarification include:

1) There are very few details on how the authors performed their subclone analysis to identify major subclones, and what each of the clusters in Supplemental Figure 1 represents. In addition, they do not describe how they determined that the highlighted mutations in Table 2 were drivers for metastasis and subclonal expansion. Were these the only genes that exhibited increased allele frequencies in metastatic sites, or were other statistical criteria used?

Thank you for the important comment about 1) clone analysis and 2) highlighted mutations in Table 2.

1) Mutations were timed as clonal or subclonal through PyClone (Roth A et al., Nat Methods. 2014) clustering (Figure 1—figure supplement 1). Phylogenetic trees were constructed using the mutation clusters identified with PyClone as an input of CITUP (Malikic S et al., Bioinformatics. 2015) (Figures 2 and 3). We added the sentence "See Supplementary File 1 to check the matching information for the PyClone clusters and the CITUP clones." to the supplementary figure legend.

2) A full list of mutations constituting a CITUP clone can be found in Supplementary File 1. Among the mutations, previously reported cancer-associated genes harboring them were selected manually and listed in Table 2. References for each gene are introduced in the 'Evolutionary trajectories and expansion of subclones during regional and distant metastasis' section.

2) The authors do not discuss the relevance of variation in mutational signatures observed with disease progression/metastasis, e.g., is there any significance that signature 22 (aristolochic acid) and signature 24 (aflatoxin) are increased in metastases? In addition, when comparing their data to previously published reports in Figure 1B and Figure 4A, it would be helpful if the authors discussed possible reasons for some of the large differences in mutational or signature frequencies across datasets. For example, do the authors think the frequency of ERBB2 alterations is so much higher in their cohort than in prior reports due to methodological/data reasons or due to differences in patient population?

Thank you for the constructive and valuable comments about 1) mutational signatures observed with disease progression/metastasis and 2) differences in mutational or signature frequencies across datasets.

1) During the revision process, signatures 22 and 24 highlighted in the metastasis stage were validated by two additional tools, Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018) (Figure 4—figure supplement 3). Aristolochic acid is an ingredient of oriental herbal medicine (Debelle FD et al., Kidney Int. 2008, Hoang ML et al., Sci Transl Med. 2013). Given that all the patients in our cohort are Korean, and a recent study found that Korean cancer patients are frequently exposed to herbal medicines (Kwon JH et al., Cancer Res Treat 2019), one possible explanation is that some patients might have been exposed to herbal remedies containing aristolochic acid. On the other hand, aflatoxin is known to be contained in soybean paste and soy sauce, which are widely used in Korean food (Ok HE et al., J Food Prot. 2007). Considering that the signatures 22 and 24 are found not in early carcinogenesis but in late carcinogenesis and metastasis (Figure 4B and Figure 4—figure supplement 3), the two carcinogens appear to have little impact on the early stage of cancer development, but their impacts might be highlighted in overt cancer cells. Further investigation is required because it is difficult to determine the etiology of signatures 22 and 24 with this limited patient data. We updated this part in the Discussion section (Page 13, Line 4-7).

2) In the two previous genomics studies on GBAC, the prevalence of ERBB2 alteration was 7.9% (Narayan RR et al., Cancer. 2019) and 9.4% (Li M et al., Nat Genet. 2014), respectively. Compared with these data, our data is characterized by relatively higher ERBB2 alterations (54.5%: amplification in 27.3% and SNV in 27.3%) (Figure 1B). A higher prevalence of ERBB2 alteration was also reported in other studies on GBAC, with corresponding rates of 28.6% (amplification and overexpression, Nam AR et al., Oncotarget. 2016) and 36.4% (amplification only, Lin J et al., Nat Commun. 2021). The variations in ethnicity and culture might have contributed to the differences. This part is described in the Discussion section (Page 11, Line 19-23). In addition, the discrepancy in Figure 4A might be attributed to the difference in analyzed samples: our study included precancerous and metastatic lesions while the other two studies uniformly analyzed primary tumors.

Reference for reply 1)

• Kwon JH, Lee SC, Lee MA, Kim YJ, Kang JH, Kim JY, et al. Behaviors and Attitudes toward the Use of Complementary and Alternative Medicine among Korean Cancer Patients. Cancer Res Treat. 2019;51(3):851-60.

3) The authors try to describe and draw conclusions about the possibility of metastasis to metastasis spread in p.6, lines 6-10 "In our study, of 7 patients with 2 or more metastatic lesions, evidence of metastasis-to-metastasis spread was found in 2 patients (28.6%). In GB-A1 (Figure 2A), it appears that CBD, omentum 1-2, mesentery, and abdominal wall 2-4 lesions may originate from abdominal wall 1 (old) rather than from primary GBAC considering clone F." The authors conclude here that the spread arose from abdominal wall 1, but this lesion is only separated from the CBD lesion by 1 month. There is no history given about whether this timing difference is significant or if it was simply due to clinically-driven differences in when each lesion was sampled. Given the proximity of the CBD lesion to the original gall bladder cancer, it seems just as likely that all of these distant lesions were seeded from the CBD lesion. If this is the case, the author's conclusion about "metastasis to metastasis" spread does not seem strongly supported. It would be helpful if the authors could clarify this point and/or provide additional data to strengthen this conclusion.

We appreciate your valuable comment. As addressed above, the manuscript has been modified to reflect your comments.

Reviewer #2 (Public Review):

Minsu Kang et al. analyzed 11 patients with gallbladder adenocarcinoma using multi-point sampling. Mutational analysis revealed evolutional patterns during progression where the authors found metastasis-to-metastasis spread and the migration of a cluster of tumor cells are common in gallbladder adenocarcinomas. The signature analysis detected signatures 22 (aristolochic acid) and 24 (aflatoxin) in metastatic tumors. Overall, the analyses are well-performed using established algorithms. However, the manuscript is highly descriptive. Therefore, it is very difficult to understand what the novel findings are.

Major comments

1) The sections "Evolutionary trajectories and expansion of subclones during regional and distant metastasis", "Polyclonal metastasis and intermetastatic heterogeneity", "Mutational signatures during clonal evolution", and "Discussion" are highly descriptive which makes it difficult to understand what the novel and/or important findings are. Those sections would profit from reorganization.

Thank you for the important comment. We have reorganized the manuscript according to your comments.

1) In the "Evolutionary trajectories and expansion of subclones during regional and distant metastasis" section, unnecessary sentences have been removed and Figures 2 and 3 have been changed to make it simpler to understand how subclones spread during metastasis.

2) In the "Polyclonal metastasis and intermetastatic heterogeneity" section, after receiving feedback on statements that were conflicting (Reviewer #1's comment 4), we clarified the statements and removed any other extraneous sentences. Figures 2 and 3 have been changed to make it simpler to understand polyclonal metastasis and intermetastatic heterogeneity.

3) In the "Mutational signatures during clonal evolution" section, after receiving comments that Figures 4B and 4C were confusing (Essential Revisions #6), we moved Figure 4B to Figure 4—figure supplement 2. Unnecessary sentences have been removed. We emphasized signatures 22 and 24 highlighted during metastasis. This result was validated by using two additional tools, Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018).

4) In the Discussion section, duplicate descriptions and unnecessary extraneous explanations have been deleted. We emphasized that whereas aflatoxin and aristolochic acid had little impact on early cancer formation, their impacts could be more clearly seen in cancer cells that had already manifested (Page 13 Line 2-7). In addition, the limitations of the NGS test currently used in the clinical field were pointed out, and the clinical significance of this study was described (Page 13 Line 8-16).

2) What would enhance this paper is more of a connection between the bioinformatics analysis and the biology. Although the authors analyzed multi-point sequencing data well, this paper lacks in-depth discussion. I understand that the results in the paper are "computationally" the most likely. However, the impact is lost by an incomplete connection to biology.

As you commented, we analyzed the WES data obtained from patient samples by computational methods. In this study, we did not validate the various results using in vitro or in vivo models. However, we would like to emphasize the significance of our work because it is the first human study, covering the current theory of carcinogenesis from precancerous lesions to metastasis in GBAC. For example, polyclonal seeding has been previously confirmed in animal models (Cheung KJ et al., Science 2016). In humans, there have been reports in breast cancer (Ullah I et al., J Clin Invest. 2018) and colorectal cancer (Wei Q et al., Ann Oncol. 2017), but not in GBAC yet.

3) In addition to the above concern, it is difficult to comprehend the cohort as the detailed information is lacking. I would suggest providing a brief table that contains the number of collected samples, frozen or FFPE, the clinical information, etc. by sample.

Thank you for the constructive comment. Supplementary Table 1 was modified as you mentioned. It is now indicated from which organ, when, and by what method the tissue was obtained, what the tumor purity of the tissue was, and whether the tissue was fresh-frozen or FFPE. In addition, we updated the information about tissue acquisition sites in Figure 1A.

4) The mutations with very low allele frequency (< 1%) are discussed in the manuscript. However, no validation data is provided. Please add a description of the accuracy of the mutation calling considering the following concerns.

• FFPE samples are analyzed using the same method as frozen samples. FFPE contains much more artifacts. Is it adequate to use the same methods for both frozen and FFPE samples?

Thank you for the valuable comment. We also considered the FFPE artifacts. However, we did not remove the possible artifacts. This part has been described above. Please see Essential Revisions #5.

• How were those mutations with low allele frequency validated? Are those variants validated by other methods? Especially in FFPE.

Thank you for the important comment. Firstly, we discarded any low-quality, unreliable reads and variants according to the pre-specified filtering criteria used in previous literature analyzed with the Genomon2 pipeline (Yokoyama A et al., Nature. 2019, Kakiuchi N et al., Nature. 2020, Ochi Y et al., Nat Commun. 2021). In the Method section, we have added an explanation for this part (Page 16 Line 5-12).

As you commented, validation of low VAF mutation is required if the mutation is sample-specific. However, in this study, if a mutation in Supplementary File 1 has a low VAF in one sample, one of the other samples always has a higher VAF, which has passed our pre-specified filter. Therefore, validation is not required for that mutation. In addition, possible sequencing artifacts with low VAFs in FFPE tissues have been discussed above. Please see Essential Revisions #5.

• Is the low variant allele frequency (0.2~1%) significantly higher than the background noise level?

Thank you for the important comment. As you expected, FFPE samples had a higher number of sample-specific mutations than fresh-frozen ones in our study. However, we did not remove these mutations in the analysis of the FFPE samples. For a more detailed description, please see Essential Revisions #5.

5) The authors compared mutational signatures divided by stages or timings. How are the signatures calculated although each sample has a distinct number of somatic mutations? Did the authors correct the difference?

Thank you for the helpful comment. We classified all the mutations according to the specific criteria (Page 9 Line 9-18). For example, in Figure 4B (before revision, Figure 4C), mutations were classified by the timing of development during clonal evolution. After that, we could calculate the relative contributions of mutational signatures in each group using the three tools, Mutalisk (Lee J et al., Nucleic Acids Res. 2018), Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018). Although the number of mutations is different for each group, no additional correction was required because we compared the relative contributions among the groups.

6) In distant metastasis tumors, signatures 22 and 24 are increased. Those two signatures are strongly associated with a specific carcinogen. Although the clinical information lacks, do the authors think that those patients were exposed to those chemicals after the diagnosis? Why do the authors think the two signatures increased in the metastatic tumors? Were those signatures validated by other methods?

We appreciate your important and constructive comment.

1) We think that the patients might have been exposed to aristolochic acid or aflatoxin before or after the cancer diagnosis. Aristolochic acid is an ingredient of oriental herbal medicine (Debelle FD et al., Kidney Int. 2008, Hoang ML et al., Sci Transl Med. 2013). Given that all the patients in our cohort are Korean, and a recent study found that Korean cancer patients are frequently exposed to herbal medicines (Kwon JH et al., Cancer Res Treat 2019), one possible explanation is that some patients might have been exposed to herbal remedies containing aristolochic acid. On the other hand, aflatoxin is known to be contained in soybean paste and soy sauce, which are widely used in Korean food (Ok HE et al., J Food Prot. 2007). Nevertheless, we believe that further investigation is required because it is difficult to determine the etiology of signatures 22 and 24 with this limited patient data.

2) Summarizing the mutational signature results using the 3 different tools (Figure 4B and Figure 4—figure supplement 3), the signatures 22 and 24 are relatively rare in early carcinogenesis. However, the two signatures contributed more to late carcinogenesis and metastasis. Therefore, it is speculated that the two carcinogens appear to have little impact on the early stage of cancer development but might be highlighted in overt cancer cells. Further studies on this novel hypothesis are necessary.

3) During the revision process, signatures 22 and 24 highlighted in the metastasis stage were validated by two additional tools, Signal (Degasperi A et al., Nat Cancer. 2020) and MuSiCa (Diaz-Gay M et al., BMC Bioinformatics. 2018) (Figure 4—figure supplement 3). We updated this part in the Result (Page 9 Line 18-21) and Discussion (Page 13 Line 2-7) sections.

Reference for reply 1)

• Kwon JH, Lee SC, Lee MA, Kim YJ, Kang JH, Kim JY, et al. Behaviors and Attitudes toward the Use of Complementary and Alternative Medicine among Korean Cancer Patients. Cancer Res Treat. 2019;51(3):851-60.

7) Figures 2 are well-described. However, they are difficult for readers to fully understand. The colors for each clone are sometimes similar. The results of multi-time point and regional analyses in the cases with multiple sampling are not integrated. Driver mutations are separately described in the small phylogenetic trees. Evolutional patterns (linear or branching) are not described in the figures. Modifying the above concerns would improve the manuscript.

We appreciate your important comment.

1) In GB-S1, clones of similar colors were modified to be different colors.

2) Figures 2 and 3 have been modified to make them easier to understand by separating time and space more clearly.

3) Driver mutations are now indicated in both the phylogenetic tree and TimeScape result (Figures 2 and 3).

4) Evolutional patterns (linear or branching) can be discovered by examining the phylogenetic tree in Figures 2 and 3. In addition, we described each patient's evolutionary pattern more clearly in the manuscript.

8)"Among 6 patients having concurrent BilIN tissues, two patients were excluded from the further analysis because of low tumor purity in one patient and different mutational profiles between BilIN and primary GBAC in the other patient, suggesting different origins of the two tumors (Figure 1-figure supplement 2)." This seems cherry-picking. More explanation is necessary.

• How is the tumor purity? Although the authors use 0.2% variant allele frequency as true mutation (for example Table 2), is the tumor purity lower than 0,2%?

Thank you for the important comment. The calculated tumor purity of BilIN in the GB-S8 patient was 0.03 based on the WES data. We added this value to the manuscript (Page 6 Line 9) and Supplementary Table 1. Although variants were called in this case, the tumor purity was too low to estimate the allele-specific copy number, and thus sophisticated analysis as in other patients was not possible. In addition, the value of 0.2% in Table 2 is not the VAF, but cellular prevalence calculated by PyClone and CITUP. Although the value is low in the primary tumor, it is mentioned because it is high in metastatic lesions.

• BilIN and GBAC of GB-S7 have some shared mutations. Why do the authors conclude that BilIN and GBAC have distinct origins? Do the authors think that those shared mutations are germline mosaic mutations?

Thank you for the important comment.

1) We think that the BilIN and GBAC of the GB-S7 patient are tumors of different origins because BilIN and GBAC of the GB-S7 patient have different truncal mutations (Figure 1—figure supplement 2C). This is a markedly different feature compared to BilIN and GBAC samples of other patients. We have added an explanation for this part to the Results section (Page 6 Line 9-11).

2) We do not think that mosaicism occurred at the developmental stage. In addition, although some mutations were identified from both BilIN and GBAC, we cannot determine their importance because either one of the lesions had a very low VAF ranging from 0.001 to 0.04. If the mosaicism occurred only in the GB at the developmental stage, the VAF values of the shared mutations should be much higher than the current values, and the VAF values of the two BilIN and GBAC lesions should be similar.

• Was the copy number profile compared between BilIN and GBAC?

Thank you for the constructive comment. In this study, we obtained allele-specific copy numbers using Control-FREEC version 11.5 (Boeva V et al., Bioinformatics. 2012). The copy number of the mutations in the GB-S8 patient's BilIN could not be estimated by Control-FREEC due to low tumor purity (0.03). In the case of GB-S7, BilIN and GBAC were determined to be of a different tumor origin and thus disregarded from the analysis.

Author Response

Reviewer #1 (Public Review):

It's here where my very mild (I truly liked this article - it is well done, well written, and creative) comments arise. The implications for stochastic strategies immediately emerge in the early results - bimodal strategies come about from the introduction of two variables. There is not enough credence given to the field of stochastic behavior in the introduction - the introduction focuses too much on previous models of predator-prey interaction, and in fact, Figure 1, which should set up the main arguments of the article, shows a model that is only slightly different (slight predator adjustment) that is eventually only addressed in the Appendix (see below). The question of "how and when do stochastic strategies emerge?" is a big deal. Figure 1 should set up a dichotomy: optimal strategies are available (i.e., those that minimize Tdiff) which would predict a single unimodal strategy. Many studies often advocate for Bayesian optimal behavior, but multimodal strategies are the reality in this study - why? Because if you consider the finite attack distance and inability of fish to evoke maximum velocity escapes while turning, it actually IS optimal. That's the main point I think of the article and why it's a broadly important piece of work. Further framing within the field of stochastic strategies (i.e., stochastic resonance) could be done in the introduction.

We appreciate the comment provided by the reviewer. We changed the second paragraph of the introduction so as to focus more on the protean tactic (stochasticity). We added a new figure (Figure 1 in the new version) to conceptually show the escape trajectories (ETs) of a pure optimal tactic, a pure protean tactic, a combination of optimal and protean tactics, and an empirically observed multimodal pattern. We explained each tactic and described that the combination of the optimal and protean tactics still cannot explain the empirically observed multiple preferred ETs.

The revised paragraph (L49-66) is as follows: Two different escape tactics (and their combination) have been proposed to enhance the success of predator evasion [16, 17]: the optimal tactic (deterministic), which maximizes the distance between the prey and the predator (Figure 1A) [4, 14, 15, 18], and the protean tactic (stochastic), which maximizes unpredictability to prevent predators from adjusting their strike trajectories accordingly (Figure 1B) [19-22]. Previous geometric models, which formulate optimal tactics, predict a single ET that depends on the relative speeds of the predator and the prey [4, 14, 15, 18], and additionally, predator’s turning radii and sensory-motor delay in situations where the predator can adjust its strike path [23-25]. The combination of the optimal tactic (formulated by previous geometric models), which predicts a specific single ET, and the protean tactic, which predicts variability, can explain the ET variability within a limited angular sector that includes the optimal ET (Figure 1C). However, the combination of the two tactics cannot explain the complex ET distributions reported in empirical studies on various taxa of invertebrates and lower vertebrates (reviewed in [26]). Whereas some animals exhibit unimodal ET patterns that satisfy the prediction of the combined tactics or optimal tactic with behavioral imprecision (e.g., [27]), many animal species show multimodal ETs within a limited angular sector (esp., 90–180°) (Figure 1D) (e.g., [4, 5, 28]). To explore the discrepancy between the predictions of the models and empirical data, some researchers have hypothesized mechanical/sensory constraints [17, 29]; however, the reasons why certain animal species prefer specific multiple ETs remain unclear.

All experiments are well controlled (I especially liked the control where you varied the cutoff distance given that it is so critical to the model). Some of the figures require more labeling and the main marquee Figure 1 needs an overhaul because (1) the predator adjustment model that is only addressed in the Appendix shouldn't be central to the main introductory figure - it's the equivalent of the models/situations in Figure 6, and probably shouldn't take up too much space in the introductory text either (2) the drawing containing the model variables could be more clear and illustrative.

(1) According to this comment and comment #11 from reviewer #2, we moved the two panels in the figure (Figure 1B and D in the original version) to Appendix-figure 1, and accordingly, we changed the first paragraph of the Model section so as to clearly describe that we focus on Domenici’s model in this study (L103-108).

As for Figure 6 (Figure 7 in the new version) and related parts, we tempered our claims to clearly describe that our model has only the potential to explain the different patterns of escape trajectories observed in previous works. We would like to keep this figure in the main text because it is fundamental to explain the potential applicability of our model to other predator-prey systems.

(2) To alleviate the burden for readers, we added the model variables to the figure and made them colored (Figure 2B in the new version).

Finally, I think a major question could be posed in the article's future recommendations: Is there some threshold for predator learning that the fish's specific distribution of optimal vs. suboptimal choice prevents from happening? That is, the suboptimal choice is performed in proportion to its ability to differentiate Tdiff. This is "bimodal" in a sense, but a probabilistic description of the distribution (e.g., a bernoulli with p proportional to beta) would be really beneficial. Because prey capture is a zero-sum game, the predator will develop new strategies that sometimes allow it to win. It would be interesting if eventually the bernoulli description could be run via a sampler to an actual predator using a prey dummy; one could show that the predator eventually learns the pattern if the bernoulli for choosing optimal escape is set too high, and the prey has balanced its choice of optimal vs. suboptimal to circumvent predator learning.

We thank the reviewer for this constructive comment. Actually, we are now developing a dummy prey system. We added the following sentence in the Discussion to mention future research.

The added sentence (L496-499): Further research using a real predator and dummy prey (e.g., [48]) controlled to escape toward an optimal or suboptimal ET with specific probabilities would be beneficial to understand how the prey balances the optimal and suboptimal ETs to circumvent predator learning.

Reviewer #2 (Public Review):

First, it is unclear how the dummy predator is actuated. The description in the Methods section does not clearly address how rubber bands are used for this purpose.

To clearly mention how the dummy predator was actuated by rubber bands, we added a figure (Figure 3-figure supplement 3B) and the following sentences.

The added sentences (L608-611): The dummy predator was held in place by a metal pipe anchored to a four-wheel dolly, which is connected to a fixed metal frame via two plastic rubber bands (Figure 3—figure supplement 3B). The wheel dolly was drawn back to provide power for the dummy predator to strike toward the prey.

Second, the predator's speed, which previous research has identified as a critical factor during predator-prey interactions, is not measured from the motion of the dummy predator in the experiments. Instead, it is estimated using an optimization algorithm that utilizes the mathematical model and the prey-specific parameters. It is unclear why the authors chose this method over measuring velocity from their experiments. Since the prey fish are responding to a dummy predator moving toward them at a particular speed during the interaction, it is important to measure the speed of the predator or clearly explain why estimating it using an optimization procedure is more appropriate.

We chose this method (optimizing predator speed from the prey’s viewpoint) because there was no significant effect of predator speed on the escape trajectory in our experiment (L203-208). In other words, we considered that, at least in our case, the prey did not change the escape trajectory in response to the predator speed, and thus it would be more appropriate to use a specific predator speed estimated through an optimization algorithm from the prey’s point of view. It may be appropriate to use measured predator speed in other cases where the prey adjusts the escape trajectory in response to the change in predator speed. Therefore, we conducted a further analysis using actual predator speeds (both the predator speed at the onset of escape response, and the mean speed for the predator to cover the distance between the predator and prey). The results show that the model fit became worse when using measured predator speed per trial compared to the model using the fixed predator speed estimated through the optimization procedure (Table 3—source data 1; Figure 5—figure supplement 1). We added the above explanation in L219-226.

One of the major claims of this article is that the model can explain escape trajectories observed in other predator-prey systems (presented in Figure 6). Figure 6 panels A-C show the escape responses of different prey in response to some threatening stimuli. Further, panels D-F suggest that the empirical data can be predicted with the model. But the modeling parameters used to produce the escape trajectories in D-F are derived from the authors' experiments with fish, instead of the experiments with the species shown in panels A-C.

We thank the reviewer for this comment. We agree that this part in the previous version was an over-interpretation. Therefore, we tempered our statements to simply suggest that our approach has the potential to explain multiple ETs observed in other taxa. The revised sentences are as follows.

Abstract (L27-30): By changing the parameters of the same model within a realistic range, we were able to produce various patterns of ETs empirically observed in other species (e.g., insects and frogs): a single preferred ET and multiple preferred ETs at small (20–50°) and large (150–180°) angles from the predator.

Results (L395-407): Potential application of the model to other ET patterns. ...(sip)... To investigate whether our geometric model has the potential to explain these different ET patterns, we changed the values of model parameters (e.g., Upred, Dattack) within a realistic range, and explored whether such adjustments can produce the ET patterns observed in the original work. ...(sip)... These results indicate that our model has the potential to explain various patterns of observed animal escape trajectories.

Discussion (L538-548): We show that our model has the potential to explain other empirically observed ET patterns (Figure 7). ...(sip)... Further research measuring the escape response in various species and applying the data to our geometric model is required to verify the applicability of our geometric model to various predator-prey systems.

Author Response

Reviewer #3 (Public Review):

The authors use two-photon imaging to visualize various axonal organelle populations that they have virally labeled with fluorescent proteins, including DCVs and late endosomes/ lysosomes. The latter topic is a bit contentious, as the authors use two labels that tag potentially overlapping and not highly specific markers so that the nature of the tagged organelle populations remains unclear. Notably, the authors also have previously published a detailed account of how DCVs traffic in vivo, so the novelty is mostly in comparing the behavior of different organelles and the potential influence of activity.

Overall, the reported results mostly corroborate the expectations from previous in vitro and in vivo work on these organelles and other cargoes, performed by the authors and their collaborators, as well as in many other laboratories:

(i) Different organelles have different transport behaviors regarding speed, the ratio of anterograde to retrograde moving organelles, etc.

(ii) Organelles move in different ways when they pass specific anatomical landmarks in the axons, such as presynaptic terminals.

(iii) Activity of a neuron (here measured by calcium imaging) can impact the measured transport parameters, albeit in a subtle and mechanistically not well-defined manner. The chosen experimental design precludes a more detailed analysis, for example of the precise movement behavior (such as defining the exact pausing/movement behavior of organelles, which would require higher imaging speeds) or of a correlation of different organellar behavior at synaptic sites or during activity (which would require three-channel simultaneous imaging of two organelle classes plus a synaptic or activity marker).

In summary, this publication uses sophisticated in vivo labeling and imaging methods to corroborate and complement previous observations on how different axonal organelles move, and what influences their trafficking.

We thank the reviewer for the time dedicated to our manuscript. We are thankful for the critical and specific comments, which allowed us to further improve our manuscript. We agree that it would have been beneficial to have higher frame rates and there instead of two imaging channels. However, this would have further added technical complexity to an already complex experimental setup resolving fluorescent puncta with sizes below the resolution limit. And we are convinced that all our main conclusions are justified based on the imaging settings in the current data sets.

Author Response:

Reviewer #2 (Public Review):

The study is well designed and provides exciting new insights into the plasticity of intracortical connections, (over-)compensating for the partial loss of thalamic inputs. To optically resolve the activity of single synapses in vivo during sensory stimulation is technically very challenging. It would be helpful to know whether the recordings were made in the binocular or monocular region of V1. The results argue against a generalized multiplicative upscaling of all inputs and suggest selective boosting of synapses that are part of sensory-driven subnetworks. However, it is not clear whether homeostatic plasticity occurred at the observed spines themselves or on the level of presynaptic neurons, which could then e.g. fire more bursts, leading to larger postsynaptic Ca transients. The possibility that thalamic inputs from the intact eye in layer 4 could be potentiated should be discussed. It would probably help to explain to the reader the layer-specific connectivity of V1 in the introduction, and why thalamic input synapses themselves were not optically monitored (may require adaptive optics). Technical limitations are a main reason why the conclusions are somewhat vague at this point ("... regulation of global responses"), this could be spelled out better.

We thank the reviewer for these suggestions. We agree with the reviewer that we cannot determine (due to technical limitations) whether the changes are occurring pre- or post-synaptically or some combination (also related to the reviewer’s point 8). We have added this point to the discussion.

"Finally, it is important to note that while we made these measurements in layer 5 pyramidal cells, the homeostatic changes mediated by TNF-α could occur outside of layer 5, including changes to upstream inputs or changes to the presynaptic responses, either through changes in presynaptic release (Vitureira et al., 2012) or through a change in activity patterns of the presynaptic cell (e.g., bursts compared to single spikes) (Linden et al., 2009)."

One important point that was unclear in the earlier version of the manuscript is that the experiments conducted in visual cortex were done in the monocular visual cortex. As explained in comments to reviewer 1, there are not any visually-evoked responses following enucleation in our experiments.

Reviewer #3 (Public Review):

Weaknesses are largely restricted to suggested changes to the writing - specifically, there are additional explanations of the data whose discussion may strengthen the long-term impact of the manuscript.

1) Most importantly, the hypothesis at the heart of this work (subset versus global processes) is framed as orthogonal to the status quo model of homeostatic processes (global). I suspect that adherents to the global argument would quickly point out that the current work is conducted in adult animals, and the majority of the homeostatic plasticity research (which forms the basis of the global model) is conducted in juvenile animals. This is an important distinction because the visual system is enriched in plasticity mechanisms during the ocular dominance critical period. Since Hubel and Wiesel at least, there is extensive evidence to suggest that sensory systems take advantage of critical periods to set themselves up in accordance with the statistics of the world in which they are embedded. The flip side of this is that sensory systems are far less readily influenced by experience once the critical period is closed (Vital-Durand et al., 1978, LeVay et al., 1980; Daw et al., 1992, Antonini et al., 1999, Guire et al., 1999, Lehmann and Lowel, 2008). Through this lens, one might predict that a key feature of the adult cortex is that sensory spines could benefit by being selectively protected from what would otherwise be global homeostatic processes. Either way, the manuscript can be read as if it is framing a show-down between the classical model and a newer, higher-resolution model. I worry that this will be interpreted as misleading without careful presentation/contextualization of the role of development in the introduction and a thorough dissection in the discussion. Currently, the first occurrence of the word, "adult", occurs in the methods, on page 27, line 512. "Juvenile" and "critical period" are not in the manuscript. The age of the animals in this study isn't mentioned until the methods (between P88 and P148 at the time of imaging).

2) Goel and Lee (2007) seem quite pertinent here: they show that L2/3 neurons give rise to homeostatic regulation of mEPSCs in both juvenile and adult animals, but that the process is no longer multiplicative in nature once the animal is post-critical period. Multiplicity has been the basis of the argument for global change since Turrigiano 1998. Thus, the Goel and Lee finding seems to really bolster the current findings - and also perhaps reconcile the likelihood of a mechanistic difference between CP and adult homeostatic plasticity.

We fully agree with the reviewer that our results are not in conflict with the developmental synaptic scaling literature. We have changed the text throughout the manuscript to highlight previous studies at different ages and made clear the age of the animals in this work (including in the abstract, introduction, results and discussion). We have also referenced Goel and Lee, 2007, which we agree should be included and thank the reviewer for pointing this out.

Author Response

Reviewer #1 (Public Review):

While eDNA methods are becoming more established, there remains skepticism by many in the scientific community about the origins of the detected DNA (e.g. does it drift in from other areas or water layers?). If these concerns aren't addressed (i.e. by citing supporting literature on the fate of eDNA), the different biodiversity profiles between trenches could possibly be explained by differing oceanography. There is also some important methodological information that is missing from this manuscript. For example, sampling volumes will affect the amount of biodiversity detected, but it is not clear if sample volumes are consistent across depths and study areas. It was also not indicated whether field controls (blanks) were taken to assess the potential contamination of samples. Lastly, the literature in the eDNA field is progressing rapidly and there are some missing papers (e.g Thomsen et al. 2016, Canals et al. 2021, McClenaghan et al. 2020, Govindarajan et al. 2021, etc.) that are relevant to the technique used in this manuscript and the habitat studied.

We are very grateful to this reviewer for providing such an in-depth review of our manuscript that allowed us to improve our manuscript significantly. We tried to follow explicitly almost every suggestion. In particular, we appreciate the input of other important missing literature that we readily included in this new version of our paper. The data on the volume of seawater filtered for each sample is given in Table Supplementary file 1a. Regarding field blanks, they were not collected per se. However, as part of the molecular protocol used (see Methodology) a “negative extraction control” was applied to check for possible contamination. Also, from the results themselves, we carefully checked for any indication of contamination that could have biased our results and conclusions.

Reviewer #2 (Public Review):

My primary critique is the near-absence of statistical analyses in the current version of the manuscript that are necessary to support the many descriptive observations made with a more formal hypothesis testing framework, as well. Developing an appropriate framework for such analyses throughout the paper, including consideration of the multiple tests that will be performed. This is important for many reasons, including by providing a more formal sense of uncertainty in the conclusions to readers, given the understandable sampling limitations. Planning and conducting these analyses will require considerable work.

We thank the reviewer for raising such concern. We did include statistical analyses in part of our work. For example, all the phylogenetic analyses (using the IQ-tree software) implicitly include statistical analyses. The calculation of the Gini index in Figure 2 is also a statistical measure. However, we agree with the reviewer that some of our results lacked statistical analysis. We thus now include statistical significance to more statements in the text and additional panels to Figure S2—figure supplement 1 (with support on data in new tables in Supplementary file 1h and 1i) to illustrate the statistical support to some of our claims. We have also removed some unnecessary statement.

Author Response

Reviewer #2 (Public Review):

This is a single RNA-seq analysis of traumatic brain injury (TBI) in mice that looks at recovery from milder TBI. It addresses an important question of why older individuals may have poor recovery. The investigators undertake unbiased analysis in both young and old mice and identify a number of macrophage, fibroblast, lymphocyte, and more specifically B cell inflammatory programs that are activated and some of which do not recover well in older mice. Taken together, these findings identify unique pathways that could be further investigated in functional studies to examine what immunologic mechanisms in the meninges may drive long-term problems from TBI. The models and analysis are well performed and compelling. This paper can serve as a resource for those who study brain immunology. Open questions include the following: 1) What exactly predisposes to such pro-inflammatory programs in the aged meninges? Epigenetic alterations?, 2) What are the effector mechanisms that negatively impact brain function, and 3) Can bioinformatic approaches reveal putative intercellular communication networks that would lend insight into the spatiotemporal sequence of events and ligand-receptor interactions?

We are glad to hear that the Reviewer finds our work compelling, well performed and that it will be a good resource for those who wish to study brain immunology. The open questions that the Reviewer brings forth are very compelling areas of future investigation that we believe will help to shape and advance this field in the coming years.

Reviewer #1 (Public Review):

In this manuscript by Feng et al., the authors investigate the mechanism regulating the development of the levator veli palatini (LVP) in the posterior palate/pharyngeal region. While set up as a model to understand how myogenic progenitors migrate to discrete sites to form individual muscles, it is not clear how applicable the findings are to other subpopulations, though this is not a weakness. The mechanisms driving LVP development are of great interest to a broad group of developmental biologists, as LVP malformation is a common problem even in mild cases of cleft palate. The authors hypothesized that the perimysial population within palatal mesenchyme cells is a niche required for pharyngeal muscle development. Using exquisite analysis of scRNA-seq data from E13.5-E15.5 palatal cells, the authors illustrate that TGFb signaling is likely involved in perimysial cell development, using gene expression analysis in wild-type palatal sections to show that TGFb signaling precedes the arrival of myogenic cells. Inactivating ALk5 in palatal mesenchyme cells results in failure of LVP formation. The authors continue by identifying a number of transcription factors that presumably function downstream of TGFb signaling that drive LVP development. Among these are Fgf18, in which SMAD sites observed in the upstream region were validated to bind Smad2/3. The authors also identify Creb5 as a potential regulator of Fgf18. Overall, this is a remarkable use of scRNA-seq data, in which findings are supported by subsequent in vivo analysis of gene function using knockout mouse models. These findings will drive further analysis of LVP development and may shed light on the myogenesis of pharyngeal muscle in general.

Strengths

1) The treatment of scRNA-seq data using a variety of bioinformatic programs illustrates the utility of this type of data when using sufficient analysis software. The description of the approach is very clear and concise and the controls appear excellent. Further, the use of multiple time points further improves the analysis.

2) The focus of perimysial cell expression patterns supports the hypothesis of the authors, though as with this type of data, one probably can make a story out of several pathways. The use of RNAscope to carefully examine where TGFb signaling in the posterior pharynx occurs between E12.5 and E16.5 is critical to the setup of this manuscript and is well done. Further aiding the interpretation of these results are cartoons associated with the staining, which illustrate where the staining is occurring, though never over-stating the observed patterns.

3) Careful histological analysis illustrates the poor myogenic differentiation in the LVP of OSr1-Cre;Alk5fl/fl embryos.

4) Identifying that TGFb is more important for regulating late perimysial cell development is important in identifying the targets of TGFb signaling.

5) The use of CellChat to identify sending and receiving cells is well done and further supports the late function of TGFb signaling, in this context working through Fgf18 and Lama4.

6) The attempt to build a signaling network again using CellChat (Figure 6) is admirable, though there are a few caveats to that approach (see below).

7) While bead implant studies have been used for 40 years, the approach of culturing a piece of the pharynx and then performing a bead implant to prove that Fgf18 can positively influence myogenic development is admirable.

Weaknesses

1) In general, the authors are careful to not suggest that staining is significant unless showing quantification, though, at several points, this is not true.

2) The authors identify five putative Smad2 sites upstream of Fgf18, using one of them in a Cut and Run assay whose results suggest enhanced Smad2/3 binding. The problem is that this likely would have worked with the other Smad sites and probably would have worked for any other putative site that one might pick. Proving that a putative site can be bound by its cognate transcription factor is not the same as proving that this occurs in vivo and is sufficient to control the process of LVP development. One would need reporter assays using that TF binding site to better support the points being made by the authors.

3) In a similar manner, the authors try to define which factors might function with TGFb signaling to regulate myogenic development. Using SCENIC, the authors found a number of genes that might be involved in perimysial fibroblast development. Of these, they illustrate that Creb5 siRNA knockdown decreases Fgf18 expression in cultured palates. The focus on Creb5 was based on it showing, "the most specific expression patterning the late perimysial cells (Figure 6H)....". In fact, Creb5 appears the most broad, appearing to be expressed across the entire LVP, not just in the area where myogenic precursors are found. Thus, any statement or discussion about Creb5 being a direct regulator of Fgf18 should be removed probably needs to be reworded. However, the second problem is that Creb5 knockdown reducing Fgf18 expression does not prove any direct regulation. Both of these are rather circuitous arguments.

4) While the disorganization of myogenic fibers in the posterior LVP is somewhat obvious, it is not as clear as the authors suggest. This change (which I believe) needs to be better quantified (length, width, area, etc.).

We thank the reviewer for these “Public Review” comments. For point 1, we have added more quantification for clarification and rephased the wording when quantification was not performed. For point 4, we added measurement to quantify the changes of volume and cross-section area of the LVP in Osr2Cre;Fgf18fl/fl mice (Figure 7M-V).

Reviewer #2 (Public Review):

In this study, the authors take advantage of unbiased scRNA-seq datasets of the developing mouse soft palate that they previously reported and performed a new bioinformatic analysis to identify differential signaling pathway activities in the heterogeneous palatal mesenchyme. They found a strong association of TGF-beta signaling pathway activity with the perimysial cells and validated through immunofluorescent detection of pSmad2, which led to their hypothesis that TGF-beta signaling in the perimysial cells might regulate palatal muscle formation. They generated and analyzed Osr2-Cre;Alk5fl/fl mice and showed those mice have cleft soft palate and disruption of the levator veli palataini (LVP) muscle. They then performed a comparative scRNA-seq analysis of the soft palate tissues from E14.5 Osr2-Cre;Alk5fl/fl and control embryos and showed that the Osr2-Cre;Alk5fl/fl embryos exhibited defects in the perimysial cells, in particular reduction in Tbx15+ perimysial fibroblasts that directly associate with the LVP muscle progenitors. The FGF18 is one of the most highly enriched signaling molecules in the perimysial cells and showed that the Osr2-Cre;Alk5fl/fl embryos exhibited reduced Fgf18 expression together with loss of MyoD+ myoblasts in the prospective LVP region. Further data showed that pSmad2 bound in the Fgf18 promoter region in the developing soft palate tissues. In addition, bioinformatic gene regulatory network analysis of the scRNA-seq data identified Creb5 as a potential tissue-specific transcription factor in the perimysial cells and RNAi knockdown assays in palatal mesenchyme culture suggested that Creb5 is required for Fgf18 expression. Further studies identified a subtle deficiency in LVP in Osr2-Cre;Fgf18fl/fl mice and showed that exogenous Fgf18 bead implantation in explants of E14 Osr2-Cre;Alk5fl/fl embryonic head increased the MyoD+ myoblast population in the prospective LVP region. The authors concluded that TGF-beta signaling and Creb5 cooperatively regulate Fgf18 to control pharyngeal muscle development. While the study used multiple complementary approaches and the data presented are solid, important questions need to be addressed to resolve reasonable alternative explanations of the data to the authors' main conclusion.

We thank the reviewer for the evaluation and suggestions. Responses to each of the suggested revisions are detailed below.

Major points:

1) TGF-beta signaling is known to be crucial for neural crest-derived palatal mesenchyme cell proliferation from E13.5 to E14.5. The Osr2-Cre;Alk5fl/fl mutant embryos exhibited obvious disruption of LVP myogenesis and reduced soft palatal shelf size at E14.5 (Fig3-Sup2A-D and Fig 4H-K). The cellular and molecular defects likely started prior to E14.5. Thus, it is important to examine at earlier stages (E13.5/E14.0) whether the palatal mesenchyme was already defective in cell proliferation/survival and/or perimysial cell marker expression, including Creb5 and Tbx15, to resolve whether the primary defect in the Osr2-Cre;Alk5fl/fl palatal mesenchyme could be a reduction in perimysial progenitor cell proliferation and/or differentiation of the myoblast-associated subset, for which Tbx15 and Fgf18hi act as marker genes rather than direct molecular targets. Furthermore, the apparent loss of Tbx15+ cells coincided with a specific reduction of Fgf18 expression in the myoblast-associated perimysial cells (Fig 4J/K versus Fig 5H-K), which raises the possibility that TGF-beta signaling regulates the differentiation of the Tbx5+ population from the mesenchymal progenitors while the reduction in Fgf18 expression might be a secondary consequence of the cellular defect. The data in Fig 6O showing a lack of significant induction of Fgf18 expression in the palatal mesenchyme culture in both control and Creb5-RNAi cells is also consistent with this alternative explanation.

We thank the reviewer for the valuable suggestion to identify the primary defects of the perimysial cells. We compared the expression of Creb5, Tbx15 and Fgf18 as well as Smoc2 in E13.5-E14.5 palatal mesenchyme from control and Osr2-Cre;Alk5fl/fl mice (Osr2Cre;Tgfbr1fl/fl mice). We found that expression of Creb5 is prominent from E13.5 to E14.5 and is not affected in Osr2Cre;Tgfbr1fl/fl mice, suggesting that Creb5 may not be a downstream factor but just a “partner” for TGF-β signaling. At E13.5, Tbx15 is not expressed, while Smoc2 is expressed extensively in the palatal mesenchyme but is not affected in the Osr2Cre;Tgfbr1fl/fl mice. In contrast, Fgf18 is expressed as early as E13.5 and this expression was already reduced in the palatal of Osr2Cre;Tgfbr1fl/fl mice relative to controls at this stage, suggesting the changes of Fgf18 expression are primary and precede changes in the perimysial populations. While the proliferation and apoptosis at E13.5 remain unchanged in Osr2Cre;Tgfbr1fl/fl mice, Smoc2 expression in the palate starts to be reduced at E14.0 in Osr2Cre;Tgfbr1fl/fl mice. This suggests that TGF-β signaling is required for the activation of Smoc2 during E13.5-E14.0. In parallel, Tbx15 expression is just starting to be activated in a few cells at E14.0 and this expression increased between E14.0-E14.5 in the control but failed to increase in Osr2Cre;Tgfbr1fl/fl mice. This suggests that TGF-β signaling is also required for the activation of Tbx15 during E14.0-E14.5. Thus, loss of TGF-β signaling leads to differentiation defects of both Smoc2+ and Tbx15+ perimysial cells. For Figure 6O, we performed a time-course experiment of TGF-β induction and found a significant increase of Fgf18 expression after 4 to 18 hours of treatment (instead of 24 hours used in previous experiments), with more obvious changes at 4 hours, confirming the early response of Fgf18 expression to TGF-β induction. These results have been added to Figure 4-figure supplement 2, Figure 5I-L, 5U, Figure 6-figure supplement 2, and Figure 6C.

2) Since the Osr2-Cre;Fgf18fl/fl mice exhibited much subtler palatal and LVP defects than the Osr2-Cre;Alk5fl/fl mice even though the latter still had a lot of Fgf18-expressing perimysial cells at E14.5, Fgf18 is likely a minor player in the TGF-beta mediated gene regulatory network regulating LVP formation. The major players acting downstream of TGF-beta signaling in the palatal mesenchyme, that control initial LVP progenitor migration to and/or proliferation in the soft palate region, remain to be identified and functionally validated. Whether and how Fgf18 directly regulates the perimysial-myoblast interaction is also not known.

We agree with the reviewer that the phenotype of Osr2-Cre;Fgf18fl/fl mice is much milder than that of Osr2-Cre;Alk5fl/fl mice, as we postulate that Fgf18 is just one of several perimysial-derived signals that may be affected. It will be of great interest to explore the function of other players in future studies. However, we are more inclined toward the possibility that there may be no single “major” player but rather a combination of many signals associated with different aspects of the muscle development. For example, loss of Fgf18 seems to mainly affect the Myf5+ cell proliferation in Osr2-Cre;Fgf18fl/fl mice (Osr2Cre;Fgf18fl/fl mice), as we do not observe any differentiation defect except the reduced muscle size. It is likely that other factors may also play specific functions in specific subpopulations as well. To clarify whether Fgf18 can directly affect the myogenic cell fate, we treated C2C12 mouse myogenic cells with exogenous FGF18 and found that this treatment could indeed significantly increase the proliferation of these cells. We have added these results to Figure 7—figure supplement 2.

3) While the title and the main conclusion of this manuscript imply a crucial role of Creb5 in the regulation of pharyngeal muscle development, there is no data supporting such a crucial role. Do Creb5-/- mice have specific defects in pharyngeal muscle development?

We thank the reviewer for this insight. We agree that it is very likely that Creb5 itself may have many roles in the regulation of palatal development or pharyngeal muscle development, given the prominent expression of Creb5 throughout soft palate development and in other myogenic sites of the pharyngeal muscles. Creb5-/- mice (reported as Cre-bpa-/- mice) die immediately after birth; however, the detailed phenotype of this mice was merely described as “data not shown” in a previous publication and defects of craniofacial development in these mice remain unclear (Maekawa et al., 2010). In this study, we focused on the role of Creb5 as a partner of TGF-β signaling, but we plan to generate a Creb5fl/fl mouse model to thoroughly evaluate Creb5’s functions in craniofacial development as an independent study following this work.

4) Data in Fig 6 are not sufficient to conclude that TGF-beta signaling and Creb5 cooperatively regulate Fgf18. The TGFb1 treatment did not significantly induce Fgf18 expression in either the control or Creb5-RNAi palate mesenchyme cells (Fig 6O). No data regarding how they act cooperatively to regulate Fgf18 expression.

We appreciate the reviewer for carefully reviewing our data. We re-evaluated the temporal response of Fgf18 expression following TGF- induction and found a significant increase of Fgf18 expression 4 hours post-treatment (instead of 24 hours post-treatment as used in previous experiments). We repeated the Creb5-siRNA treatment experiment using the new experimental condition and replaced the previous Figure 6O with new results showing a significant increase of Fgf18 after TGF-β induction, which was attenuated by Creb5-RNAi treatment, suggesting a requirement of Creb5 for TGF-β-mediated Fgf18 expression. The new result is now included in Figure 6Q.

Reviewer #3 (Public Review):

In this study, the authors investigated cell-cell communication between perimysial cells and skeletal muscle progenitors during soft palate development in the mouse. The authors have previously reported on the development of this structure and here they propose that a TGF-β signaling and Creb5 act to regulate Fgf18, and this pathway regulates pharyngeal muscle development through the indicated cell populations. The study is of high quality, very nicely illustrated, and uses multiple approaches including inferences from single cell transcriptomics, validations on sections, and lineage-specific gene activations. In addition, the authors successfully optimized an organ culture system from thick sections to test locally the role of FGF signaling (bead implantation). The results largely confer with the conclusions and provide a valuable example of how subjacent cell populations cooperate to establish an embryonic structure.

We thank the reviewer for the evaluation and suggestions.

Author Response

Reviewer #3 (Public Review):

The PCNT gene is found on human chromosome 21, and the same group previously showed that its increased expression is associated with reduced trafficking to the centrosome and reduced cilia frequency, which suggests a possible connection between cilia and ciliary trafficking, SHH signaling, and Down syndrome phenotypes. Jewett et al build upon this prior work by closely examining the trafficking phenotypes in cellular models with different HSA21 ploidy, or its mouse equivalent, thereby increasing the copy number of PCNT (3 or 4 copies of HSA21). They show that most of the trafficking defects can be reversed through the knockdown of PCNT in the context of HSA21 polyploidy. They also begin to examine the in vivo consequences of these trafficking disruptions, using a mouse model (Dp10) that partially recapitulates trisomy 21, including an increased copy number of PCNT. While I think this work advances our understanding of the trafficking defects caused by increased PCNT and has significant implications for our understanding of the cellular basis of a major hereditary human disorder, some improvements can be made to strengthen the conclusions and improve readability.

Major points:

I'm a little confused by the authors' conclusion that the increased PCNT levels in T21 and Q21 result in delayed but not attenuated ciliogenesis. The data show lower percentages of ciliated cells at all time points analyzed (Fig 1E) by quite a large margin in both T21 and Q21. Do the frequencies of cilia in the T21 or Q21 cells ever reach the same level as D21, say after 48-72 hours? If not it seems like not simply a delay. A bit more clarity about this point is needed.

We have now performed a ciliation time course in RPE1 D21, T21, and Q21 cells over 7 days. Our new data confirms that increasing HSA21 dosage delays but does not abolish ciliogenesis (Fig S1H). By day 3 of serum depletion, D21 and T21 cells reach similar ciliation frequencies, and after 4 days all three cell lines reach similar ciliation frequencies.

The in vivo analysis of the cerebellum was interesting and important but it felt a bit incomplete given that it was a tie between the cell biology and a specific DS- associated phenotype. For example, it is interesting that the EGL of the P4 Dp10 pups is thinner. Does this translate into noticeable defects in cerebellar morphology later? Is there a reduction in proliferation that follows the reduced cilia frequency? I think it would be possible to look at the proliferation and cerebellar morphology at some additional stages without becoming an overly burdensome set of experiments. At a minimum, are there defects in cerebellar morphology at P21 or in the adult mice? The authors allude to developmental delays in these animals - maybe that complicates the analysis? But additional exploration and/or discussion on this point would help the paper.

We have now analyzed P21 animals and found no significant differences in ciliation frequency or gross cerebellar morphology at this age. This is consistent with our new tissue culture data demonstrating that HSA21 ploidy delays but does not abolish ciliogenesis. We cannot rule out long term changes in neuronal processes or glial cells, but we believe this analysis is outside the scope of this paper.

It was a bit unclear to me why specific cell lines were used to model trisomy 21 and why this changed part way through the paper. I understand the justification for making the Dp10 mice- to enable the in vivo analysis of the cerebellum, but some additional rationale for why the RPE cell line is initially used and then the switch back to mouse cells would improve readability.

The rationale for switching to MEFs was twofold. First, Shh ciliary signaling cannot be easily studied in RPE1 cells. Therefore, ciliary function via Smoothened localization or GLI1 transcription, needed to be performed in a different cell line and the most commonly used line is MEFs. Second, the Dp mice allowed us to tease apart contributions to cilia defects from separate regions of HSA21. We have worked to clarify this point in the text.

Author Response

Reviewer #2 (Public Review):

Grasses develop morphologically unique stomata for efficient gas exchange. A key feature of stomata is the subsidiary cell (SC), which laterally flanks the guard cell (GC). Although it has been shown that the lateral SC contributes to rapid stomatal opening and closing, little is known about how the SC is generated from the subsidiary mother cell (SMC) and how the SMC acquires its intracellular polarity. The authors identified BdPOLAR as a polarity factor that forms a polarity domain in the SMC in a BdPAN1-dependent manner. They concluded that BdPAN1 and BdPOLAR exhibit mutually exclusive localization patterns within SMCs and that formative SC division requires both. Further mutant analysis showed that BdPAN1 and BdPOLAR act in SMC nuclear migration and the proper placement of the cortical division site marker BdTANGLED1, respectively. This study reveals a unique developmental process of grass stomata, where two opposing polarity factors form domains in the SMC and ensure asymmetric cell division and SC generation.

The findings of this study, if further validated, are novel and interesting. However, I feel that the data presented in the current manuscript do not fully support some crucial conclusions. The lack of dual-color images is the weakest point of this study. If it is technically impossible to add them, alternative analyses are needed to validate the main conclusions.

1) Is BdPOLAR-mVenus functional? Although the authors interpret that weak BdPOLAR-mVenus expression partially rescued the bdpolar mutant phenotype in Fig. S4D, the localization pattern visualized by BdPOLAR-mVenus may not be completely reliable with this partial rescue activity.

This is indeed a valid point. The partial complementation of weakly expressing translational reporters (Figure 3–figure supplement 1D) and the weak effect of BdPOLAR-mVenus overexpression lines (Figure 3–figure supplement 1J) at least suggest partial functionality which is strongly dependent on dosage. Yet the localization pattern and the temporal dynamics might indeed not fully reflect the spatiotemporal dynamics of the endogenous BdPOLAR. This criticism is, however, true for any transgenic reporter line–even when fully complementing–as the requirement for dosage, stability, and turnover likely varies strongly between different protein classes and functions.

Nonetheless, we have added a sentence on p. 7, which mentions this potential caveat.

2) Regardless of the functionality of the tagged protein, the authors need to provide more information on their localization. For example, is there a difference in polarity pattern depending on expression level? Does overexpressed BdPOLAR-mVenus invade the BdPAN1 zone? In such cases, might the loss of BdPOLAR polarity in the bdpan1 mutant be a side effect of overexpression, not PAN1 exclusion? Does BdPOLAR expression (no tag) show a dose-dependent effect, similar to the mVenus-tagged protein?

The difference in polarity patterns in bdpan1 mutants and wild-type does not depend on expression level. BdPOLAR-mVenus was crossed into bdpan1 and mutant and wild-type siblings in the F2 generation were analyzed. This means that the data presented in Fig. 3E and F show exactly the same transgene insertion line in wt and bdpan1 and were imaged with the same setting for comparability. Therefore, the difference in localization is not due to different expression levels but indeed reflects a PAN1-dependent effect.

To address if BdPOLAR without a tag is also sensitive to dosage, we have generated an untagged complementation line that includes the untagged, genomic locus of BdPOLAR including promoter (-3.1kb) and terminator (+1.1kb). Yet, even though this construct is much better at rescuing the mutant, we still see remaining defects in T0 lines (Figure 3–figure supplement 1K) suggesting that even without a tag we cannot fully recapitulate wild-type functionality. Yet, to actually measure protein levels of untagged BdPOLAR, we would need to raise an antibody against BdPOLAR, which we think is clearly out of the scope of this study.

3) A major conclusion of this study was that the polarity domains of BdPOLAR and BdPAN1 are mutually exclusive. However, not all the cells in the figures were consistent with this statement. For example, the BdPOLAR signals at the GMC/SMC interphase appear to match BdPAN1 localization (compare 0:03 s in Video 1 and 0:20 s in Video 2 [top cell]). The 3D rendered image in Fig. 2F shows that BdPOLAR is excluded near the GMC on the front side of the SMC, where BdPAN1 is not localized. Some cells did not exhibit polarization (Fig. 3A, bottom left; Fig. 3E, bottom left). The most convincing data are the dual-color images of these two proteins. Otherwise, a sophisticated image analysis is required to support this conclusion.

We agree that dual-color image analysis would have provided the most convincing data. As mentioned in our answers to the reviewing editor and reviewer 1, we have generated a dual marker line (BdPAN1p:BdPAN1-CFP; BdPOLARp:BdPOLAR-mCitrine), yet the BdPAN1-CFP signal (compared to mCitrine signal) was too weak to visualize the proximal BdPAN1 domain.

This issue was also raised by reviewer 1 and deemed an essential revision. To determine how BdPOLAR and BdPAN1 relate spatially to each other, we have added data in Figure 2E where we manually traced mature SMC outlines to determine BdPOLAR-mVenus and BdPAN1-mCitrine occupancy along the SMC’s circumference. This confirmed that the polarization is indeed opposite yet not perfectly reciprocal (see details above, Essential Revisions #1).

Finally, we realized that the 3D image renderings were more confusing than helpful and we removed them from the revised version.

4) Another central conclusion was that BdPOLAR was excluded at the future SC division site, marked with BdTANGLED1. However, these data are also not very convincing, as such specific exclusion cannot be seen in some figure panels (e.g., Fig. 3A, bottom left; Fig. 3E, all three cells on the left). If dual-color imaging is not feasible, a quantitative image analysis is needed to support this conclusion.

As for point 3, this was also criticized by reviewer 1 and deemed an essential revision by the reviewing editor.

To determine whether the absence of BdPOLAR signal and the presence of BdTAN1 signal colocalize, we again manually traced mature SMC outlines to determine BdPOLAR-mVenus and BdTAN1-mCitrine occupancy along the SMC’s circumference. We plotted the relative average fluorescence intensity in Figure 4G-I nicely showing that BdTAN1 indeed resides in the BdPOLAR gaps above and below the GMC (again, details above, Essential Revisions #2).

5) I could not find detailed imaging conditions and data processing methods. Are Figs. 2B and 2E max-projection or single-plane images? If they are single-plane images, which planes of the SMC are observed? In addition, how were Figs. 2C and 2F rendered? (e.g., number of images, distance intervals, processing procedures). This information is important for data interpretations.

We agree that we might not have provided sufficient imaging condition details and have added more details regarding image acquisition in the method part (p. 20). We always use a consistent depth and show the midplane of SMCs. As mentioned above, we removed Figs. 2C and 2F and the supplemental movies as these data did not seem to be helpful.

6) [Minor point] The authors should clearly describe where BdPAN1 is expressed and localized. Is it expressed in the GMC and localized at the GMC/SMC interface? Alternatively, is it expressed and localized in the SMC?

BdPAN1 is expressed throughout the epidermis but starts to strongly accumulate at the GMC/SMC interface. According to the literature (Cartwright et al 2009 with immunostainings against ZmPAN1 and Sutimantanapi et al. 2014 with PAN1 and PAN2 reporter) and our own observations (Fig. S3), this accumulation occurs in the SMC rather than in the GMC. In Fig. S3A, third panel, second GMC from the top, for example, one can see that the early PAN1 polarity domain expands beyond the GMC/SMC interface suggesting that it is indeed forming in SMCs rather than in GMCs. We have specified this in the text more clearly now (p. 5).

Author Response

Reviewer #1 (Public Review):

The research investigates the genetic basis for resistance to high CO2 levels in the human pathogenic fungus Cryptococcus neoformans. Screening collections of over 5,000 gene deletion strains revealed 96 with impaired growth, including a set of genes all related to the same RAM signaling pathway. Further genetic dissection was able compellingly to place where this pathway lies relative to upstream inputs and through the isolation of suppressor mutants as potential downstream targets of the pathway. Given the high levels of CO2 encountered by fungi in the human host, this work may provide new directions for the control of disseminated fungal disease.

The research presents both strengths and weaknesses.

Strengths include:

(1) One of the largest scale analyses of genes involved in growth under high CO2 concentrations in a fungus, revealing a set of just under 100 mutants with impaired growth.

(2) Elegant genetic epistasis analysis to show where different components fit within a pathway of transmission of CO2 exposure. For example, over expression of one of the kinases, Cbk1, can overcome the CO2-sensitivity of mutations in the CDC24 or CNA1 genes (but not in the reciprocal overexpression direction).

(3) Isolation of suppressor mutations in the cbk1 background, now able to grow at high CO2 levels, was able to lead to the identification of two genes. Follow up characterization, which included examining in vitro phenotypes, gene expression analysis, and impact during mouse infection was able to reveal that the two suppressors restore a subset of the phenotypes impacted by mutation of CBK1. Indeed, one conclusion from this careful work is that the reduced virulence of the cbk1 mutant is not due to its sensitivity to high levels of CO2, perhaps an unexpected finding given the original goals of the study towards linking CO2 sensitivity with decreased virulence.

Weaknesses include:

(1) What is the rationale for examining gene expression using the NanoString technology of 118 genes rather than a more genome-wide approach such as RNA-sequencing?

(2) Without additional species examined, some of the conclusions about differences in impact between ascomycetes and basidiomycetes might instead reflect differences between species. For example, RAM mutants in other strains of C. neoformans do not exhibit so strong a temperature sensitive phenotype. Or to extend the comparison further, one might assume given the use of CO2 for Drosophila manipulations that the RAM pathway components in an insect would not be required for surviving high CO2.

(3) Given the relative ease of generate progeny of this species, it would have been informative to explore if the suppressors of cbk1 also suppressed the loss of genes like CDC24, CNA1, etc, equivalent to the experiment performed of overexpression of CBK1 in those backgrounds.

We thank the reviewer for the kind summary of our work and the highlights of the major findings. We chose NanoString because we have already generated a probe set of 118 genes that are differentially expressed in response to CO2 based on RNA-seq profiles of multiple natural cryptococcal isolates in a separate study. Nanostring allowed us to focus on CO2 relevant transcripts and do multiple replicates and conditions in a way that is not practical using RNA-Seq.

Although the RAM pathway has not been extensively characterized in different species of Cryptococcus, we do know that RAM pathway mutants lead to pseudohyphal growth in multiple strain backgrounds including two different species of Cryptococcus (Magditch, Liu, Xue, & Idnurm, 2012; Walton, Heitman, & Idnurm, 2006). We have added corresponding references and discussed this point on lines 167-169.

We agree with the reviewer that it would be interesting to test the effects of the cbk1Δ suppressor mutations in the backgrounds of other CO2-sensitive gene knockout strains. This is part of our plan for future investigation in characterizing the signaling pathways involved in CO2 tolerance.

Reviewer #2 (Public Review):

In the paper by Chadwick et al., the authors identify the molecular determinants of CO2 tolerance in the human fungal pathogen Cryptococcus neoformans. The authors have screened a collection of deletion mutants to identify the genes that are sensitive at 37oC (host temperature) and elevated CO2 levels. The authors identified that the genes responsible for CO2 sensitivity are involved in the pathways responsible for thermotolerance mechanisms such as Calcineurin, Ras1-Cdc24, cell wall integrity, and the Regulator of Ace2 and Morphogenesis (RAM) pathways. Moreover, they identified that the mutants of the RAM pathway effector kinase Cbk1 were most sensitive to elevated temperature and CO2 levels. This study uncovers the previously unknown role of the RAM pathway in CO2 tolerance. Transcriptome data indicates that the deletion of CBK1 results in an alteration in the expression of CO2-related genes. To identify the potential downstream targets of Cbk1, the authors performed a suppressor screen and obtained the spontaneous suppressor mutants that rescued the sensitivity of cbk1 mutants to elevated temperature and CO2. Through this screen, the authors identified two suppressor groups that showed a modest improvement in growth at 37˚C and in presence of CO2.

Interestingly, from the suppressor screen, the authors identified a previously known interactor of Cbk1 which is SSD1, and an uncharacterized gene containing a putative Poly(A)-specific ribonuclease (PARN) domain named PSC1 (Partial Suppressor of cbk1Δ) which acts downstream of Cbk1. Deletion of these two genes in cbk1 null mutants rescued the sensitivity to elevated CO2 levels and temperature but did not fully rescue the ability to cause disease in mice.

This study highlights the underappreciated role of the host CO2 tolerance and its importance in the ability of a fungal pathogen to survive and cause disease in host conditions. The authors claim to gain insight into the genetic components associated with carbon dioxide tolerance. The experimental results including the data presented, and conclusions drawn do justice to this claim. Overall, it is a well-written manuscript. However, some sections need improvement in terms of clarity and experimental design.

• One major drawback of the study is the virulence assay performed to test the ability of cbk1 mutants to cause the disease in the mouse model. The cbk1 null mutants are thermosensitive in nature. Using these mutants, establishing the virulence attributes in mice would undermine the mutants' ability to infect mice as they won't be able to survive at the host body temperature.

• The rationale for choosing the genes to test further is not clear in two instances in the study. a) From a list of 96 genes, how do the authors infer the pathways involved? Was any pathway analysis performed that helped them in shortlisting the pathways that they subsequently tested? A GO term analysis of the list of genes identified through the genetic screen would be more helpful to get an overview of the pathways involved in CO2 tolerance. b) The authors do not clearly mention why they chose only four genes to test for the CO2 sensitivity out of 16 downregulated genes identified from the nano string analysis.

• It would be more useful to the readers if the authors could also include a thorough analysis of the presence of the putative PARN domain-containing protein across various fungal species rather than mentioning that it is only observed in C. neoformans and S. pombe. Also, the authors may want to discuss the known role(s) of SSD1, if any, in pathogenic ascomycetous yeasts so that the proposed functional divergence is supported further.

We are glad that the reviewer appreciated the approach, the findings, and the significance of this research, and we are grateful for the helpful suggestions to improve the manuscript.

To remove temperature sensitivity as a variable when testing virulence, we have added a new infection model in the revised manuscript to test the cbk1Δ mutant and its suppressors. This infection model uses the Galleria mellonella larvae as a host. G. mellonella larvae are commonly used to test virulence for temperature sensitive strains as the body temperature of the larvae is similar to that of the environment. We performed cryptococcal infection in this model and the larvae were kept at 30°C rather than at 37°C. The results of these experiments are now described in results section 5 and shown in Figure 6 of the manuscript. The data using the larva-infection model supports our original conclusion about the virulence of these strains observed in mouse models.

We performed a GO term analysis of the hits from our screening, but did not find any significant or outstanding pathways. From our list of 96 genes, we chose to focus on the RAM pathway because the mutants were among the most sensitive to CO2. We have added an explanation for the genes we decided to test for host CO2 level sensitivity from the 16 downregulated genes on lines 139-141.

Through Blast searching, we have found that the PARN domain-containing protein has homologs in other basidiomycetes. There might be some homologs in a few zygomycetes and ascomycetes but the confidence scores were so low that we deemed unlikely. We now report this in the manuscript on lines 210-213, “This domain was previously reported to be found in S. pombe (Marasovic, Zocco, & Halic, 2013). Interestingly, through a Blast search of the PARN domain, we did not identify this domain in the genomes of S. cerevisiae, C. albicans or other ascomycetes, but found it in Basidiomycetes and higher eukaryotes”.

Ssd1 has been studied in the pathogenic yeast Candida albicans and is also regulated by Cbk1 in this organism. We have added a discussion about possible functions of Ssd1 in C. neoformans based on references to studies in C. albicans in the discussion section on lines 401-408. “In C. albicans, Ssd1 plays an important role in polarized growth and hyphal initiation by negatively regulating the transcription factor Nrg1 (H. J. Lee, Kim, Kang, Yang, & Kim, 2015). The observation that cbk1Δpsc1Δ and cbk1Δssd1Δ suppressor mutants partially rescue cell separation defects or depolarized growth suggests that C. neoformans may primarily utilize Ssd1/Psc1 rather than a potential Ace2 homolog to regulate cell separation or polarization. Differential regulation of target mRNA transcripts by Ssd1 and Psc1 may explain the functional divergence of the RAM pathway we observed here between basidiomycete Cryptococcus and the ascomycete yeasts.”

Reviewer #3 (Public Review):

In this work the authors identify genes and pathways important for CO2 and thermotolerance in Cryptococcus neoformans. They additionally rule out the contribution of the bicarbonate or cAMPdependent activation of adenylyl cyclase to this pathway, which is important for CO2 sensing in other fungi, further solidifying the need to characterize CO2 sensing in basidiomycetes. The authors establish the importance of focusing on CO2 tolerance by testing the impact of CO2 on fluconazole susceptibility with varied pH, suggesting the ability of CO2 to sensitize cryptococcal cells to fluconazole. Furthermore, the authors compared the CO2 tolerance of clinical reference strains to environmental isolates. The characterization of the RAM pathway Cbk1 kinase illustrated the integration of multiple stress signaling pathways. By using a series of CBK1OE insertions in strains with deletions in other pathways, the ability of Cbk1 over-expression to rescue several strains from CO2 sensitivity was apparent. Additionally, NanoString expression analysis comparing cbk1∆ to H99 validated the author's screen of CO2-sensitive mutants as 16/57 downregulated genes were found in their screen, further confirming the interconnected nature of these pathways. The importance of the RAM pathway in maintaining CO2 and thermotolerance was also incredibly clear.

Perhaps most interestingly, the authors identify suppressor colonies with distinctive phenotypes that allowed for the characterization of downstream effectors of the RAM pathway. These suppressor colonies were found to have mutations in SSD1 and PSC1 which somewhat restore growth at 37oC with CO2 exposure. Further confirming the importance of the RAM pathway, the cbk1∆ strain had markedly attenuated virulence during infection. Interestingly, the generated suppressor strains had varying impacts on fungal infection in vivo. While the sup1 suppressor was completely cleared from the lungs during both intranasal and IV infection, the sup2 strain, containing mutations in SSD1, maintained a high fungal load in the lungs and was able to disseminate into host tissues during IV infection but not intranasal infection.

The authors make a strong case for the exploration of thermotolerance and CO2 tolerance as contributors to virulence. Through screening and characterization of RAM pathway kinase CBK1's ability to rescue other mutants from CO2 sensitivity, the overlapping contributions of several signaling pathways and the importance of this kinase were revealed. This work is important and will be valuable to the field. However, the cbk1∆ strain does show reduced melanization, urease secretion, and higher sensitivity to cell wall stressor Congo Red in SI Appendix, Figure S4. While the authors make a strong argument that these well-established virulence factors are not perfect predictors of virulence in vivo, the cbk1∆ strain is not an example of such a case as it does have defects in these important factors in addition to thermotolerance and CO2 tolerance. Not acknowledging the changes in these virulence factors in the cbk1∆ and their potential contribution to phenotypes observed is a weakness of the manuscript. Interestingly, the sup1 and sup2 strains also rescue these virulence factors compared to cbk1∆. Additionally, the assertion that "the observation that only sup2 can survive, amplify, and persist in animals stresses the importance of CO2 tolerance in cryptococcal pathogens" due to the sup2's slightly higher CO2 tolerance compared to sup1, could be better supported by the data. These suppressors did not restore transcript abundances of the differentially expressed genes to WT levels, suggesting post-transcriptional regulation. However, there may be differences in the ability of sup2 to resist stress better than sup1 especially given the known Ssd1 repression of transcript translation in S. cerevisiae. Finally, pH appears to impact the sup1 and sup2 strain's sensitivity to CO2 in SI Appendix Figure 4. This could be better explained and interrogated in the manuscript. Finally, this work includes a variety of genes in several signaling pathways. The paper would be greatly clarified by a graphical abstract indicating how CBK1 may be integrating these pathways or by indicating which genes belong to which pathways in the Figure 1 legend to make this figure easier to follow.

We thank the reviewer for the thorough summary of the study. We appreciate the reviewer’s enthusiasm about this study as well as constructive critiques on the manuscript. Indeed, the suppressor mutations in the cbk1Δ mutant rescue more phenotypes of cbk1Δ in vitro than just thermotolerance and CO2 tolerance (Supplemental Figure 5), which could benefit the survival of these suppressor strains in vivo compared to the original the cbk1Δ mutant. However, between the sup1 and the sup2 mutants, the only clear difference in growth we observed was in host levels of CO2 and temperature. There was no obvious difference in their resistance to Congo red (cell wall stress), melanization, susceptibility to FK506 (calcineurin pathway inhibitor), sensitivity to H2O2 (ROS), or urease (Supplemental Figure 5). Nonetheless, we agree with the reviewer that there could be other reasons which may influence the outcome in vivo, given that the host environment is more complex than we know. We have changed our wording in the manuscript to make it clear that contribution of better tolerance of CO2 to better survival of the sup2 mutant is only our hypothesis and there could be other unrecognized contributing factors. “The only in vitro difference observed between sup1 and sup2 was better growth of sup2 at host CO2 levels which may explain the difference in their ability to propagate and persist in the mouse lungs. However, due to the complexity of the host environment, there could be other unrecognized factors contributing to their growth difference in vivo.” (Lines 276279).

About growth at different pH levels, C. neoformans tends to grow better at lower pH, closer to pH 5. This fungus can grow at pH 3, the lowest pH that our lab had tested (it may be able to sustain viability even at pH 2 based on others’ conference presentations). The high temperature/CO2 combined with neutral or high pH likely causes worse growth of both H99 and the mutants tested.

We tried making a model to integrate all the pathways and factors identified in this work as the reviewer suggested. However, in this process, we found it difficult to propose a model. Although the current findings clearly demonstrate the importance of Cbk1 in thermotolerance and CO2 tolerance (overexpression of CBK1 can partially restore thermotolerance and/or CO2 tolerance in the mutants defective in the cell wall integrity pathway, the calcineurin pathway or the Cdc24-Ras1 pathway, and that the reciprocal overexpression of these genes in the cbk1∆ mutant does not rescue any of the cbk1∆ mutant’s defects), we do not know the exact mechanisms underlying this phenomenon. Do these pathways directly interact with Cbk1, affect its phosphorylation status, or alter its subcellular localization? Or do these pathways act through some other massagers to indirectly activate Cbk1 or maybe Cbk1’s downstream targets? These are the questions that warrant further investigations in the future. To be prudent, we think it is better not to propose a model at this point given the uncertainty of the mechanism. The mutants belonging to each of the pathways are clearly specified in the texts in this revised manuscript to help orient the readers. For example “As the RAM pathway effector kinase mutant cbk1Δ showed the most severe defect in thermotolerance and CO2 tolerance compared to the mutants of the other pathways, we first overexpressed the gene CBK1 in the following mutants, cdc24∆ (Ras1-Cdc24), mpk1∆ (CWI), cna1∆ (Calcineurin), and the cbk1Δ mutant itself, and observed their growth at host temperature and host CO2 (Figure 2B)...”

Author Response

Public Evaluation Summary:

The authors re-analyzed a previously published dataset and identify patterns suggestive of increased bacterial biodiversity in the gut may creating new niches that lead to gene loss in a focal species and promote generation of more diversity. Two limitations are (i) that sequencing depth may not be sufficient to analyze strain-level diversity and (ii) that the evidence is exclusively based on correlations, and the observed patterns could also be explained by other eco-evolutionary processes. The claims should be supported by a more detailed analysis, and alternative hypotheses that the results do not fully exclude should be discussed. Understanding drivers of diversity in natural microbial communities is an important question that is of central interest to biomedically oriented microbiome scientists, microbial ecologists and evolutionary biologists.

We agree that understanding the drivers of diversity in natural communities is an important and challenging question to address. We believe that our analysis of metagenomes from the gut microbiomes is complementary to controlled laboratory experiments and modeling studies. While these other studies are better able to establish causal relationships, we rely on correlations – a caveat which we make clear, and offer different mechanistic explanations for the patterns we observe.

We also mention the caveat that we are only able to measure sub-species genetic diversity in relatively abundant species with high sequencing depth in metagenomes. These relatively abundant species include dozens of species in two metagenomic datasets, and we see no reason why they would not generalize to other members of the microbiome. Nonetheless, further work will be required to extend our results to rarer species.

Our revised manuscript includes two major new analyses. First, we extend the analysis of within-species nucleotide diversity to non-synonymous sites, with generally similar results. This suggests that evolutionarily older, less selectively constrained synonymous mutations and more recent non-synonymous mutations that affect protein structure both track similarly with measures of community diversity – with some subtle differences described in the manuscript.

Second, we extend our analysis of dense time series data from one individual stool donor and one deeply covered species (B. vulgatus) to four donors and 15 species. This allowed us to reinforce the pattern of gene loss in more diverse communities with greater statistical support. Our correlational results are broadly consistent with the predictions of DBD from modeling and experimental studies, and they open up new lines of inquiry for microbiome scientists, ecologists, and evolutionary biologists.

Reviewer #1 (Public Review):

This paper makes an important contribution to the current debate on whether the diversity of a microbial community has a positive or negative effect on its own diversity at a later time point. In my view, the main contribution is linking the diversity-begets-diversity patterns, already observed by the same authors and others, to genomic signatures of gene loss that would be expected from the Black Queen Hypothesis, establishing an eco-evolutionary link. In addition, they test this hypothesis at a more fine-grained scale (strain-level variation and SNP) and do so in human microbiome data, which adds relevance from the biomedical standpoint. The paper is a well-written and rigorous analysis using state-of-the-art methods, and the results suggest multiple new experiments and testable hypotheses (see below), which is a very valuable contribution.

We thank the reviewer for their generous comments.

That being said, I do have some concerns that I believe should be addressed. First of all, I am wondering whether gene loss could also occur because of environmental selection that is independent of other organisms or the diversity of the community. An alternative hypothesis to the Black Queen is that there might have been a migration of new species from outside and then loss of genes could have occurred because of the nature of the abiotic environment in the new host, without relationship to the community diversity. Telling the difference between these two hypotheses is hard and would require extensive additional experiments, which I don't think is necessary. But I do think the authors should acknowledge and discuss this alternative possibility and adjust the wording of their claims accordingly.

We concur with the reviewer that the drivers of the correlation between community diversity and gene loss are unclear. Therefore, we have now added the following text to the Discussion:

“Here we report that genome reduction in the gut is higher in more diverse gut communities. This could be due to de novo gene loss, preferential establishment of migrant strains encoding fewer genes, or a combination of the two. The mechanisms underlying this correlation remain unclear and could be due to biotic interactions – including metabolic cross-feeding as posited by some models (Estrela et al., 2022; San Roman and Wagner, 2021, 2018) but not others (Good and Rosenfeld, 2022) – or due to unknown abiotic drivers of both community diversity and gene loss.”

Additionally, we have revised Figure 1 to show that strain invasions/replacements, in addition to evolutionary change, could be an important driver of changes in intra-species diversity in the microbiome.

Another issue is that gene loss is happening in some of the most abundant species in the gut. Under Black Queen though, we would expect these species to be most likely "donors" in cross-feeding interactions. Authors should also discuss the implications, limitations, and possible alternative hypotheses of this result, which I think also stimulates future work and experiments.

We thank the reviewer for raising this point. It is unclear to us whether the more abundant species would be donors in cross-feeding interactions. If we understand correctly, the reviewer is suggesting that more abundant donors will contribute more total biomass of shared metabolites to the community. This idea makes sense under the assumption that the abundant species are involved in cross-feeding interactions in the first place, which may or may not be the case. As our work heavily relies on a dataset that we previously analyzed (HMP), we wish to cite Figure S20 in Garud, Good et al. 2019 PLoS Biology in which we found there are comparable rates of gene changes across the ~30 most abundant species analyzed in the HMP. This suggests that among the most abundant species analyzed, there is no relationship between their abundance and gene change rate.

That being said, we acknowledge that our study is limited to the relatively abundant focal species and state now in the Discussion: “Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome.”

Regarding Figure 5B, there is a couple of questions I believe the authors should clarify. First, How is it possible that many species have close to 0 pathways? Second, besides the overall negative correlation, the data shows some very conspicuous regularities, e.g. many different "lines" of points with identical linear negative slope but different intercept. My guess is that this is due to some constraints in the pathway detection methods, but I struggle to understand it. I think the authors should discuss these patterns more in detail.

We sincerely thank the reviewer for raising this issue, as it prompted us to investigate more deeply the patterns observed at the pathway level. In short, we decided to remove this analysis from the paper because of a number of bioinformatics issues that we realized were contributing to the signal. However, in support of BQH-like mechanisms at play, we do find evidence for gene loss in more diverse communities across multiple species in both the HMP and Poyet datasets. Below we detail our investigation into Figure 5b and how we arrived at the conclusion that is should be removed:

(1) Regarding data points in Figure 5B where many focal species have “zero pathways”,we firstly clarify how we compute pathway presence and richness. Pathway abundance data per species were downloaded from the HMP1-2 database, and these pathway abundances were computed using HUMAnN (HMP Unified Metabolic Analysis Network). According to HUMAnN documentation, pathway abundance is proportional to the number of complete copies of the pathway in the community; this means that if at least one component reaction in a certain pathway is missing coverage (for a sample-species pair), the pathway abundance may be zero (note that HUMAnN also employs “gap filling” to allow no more than one required reaction to have zero abundance). As such, it is likely that insufficient coverage, especially for low-abundance species, causes many pathways to report zero abundance in many species in many samples. Indeed, 556 of the 649 species considered had zero “present” pathways (i.e. having nonzero abundance) in at least 400 of the 469 samples (see figure below).

(2) We thank the reviewer for pointing out the “conspicuous regularities” in Figure 5B,particularly “parallel lines” of data points that we discovered are an artifact of the flawed way in which we computed “community pathway richness [excluding the focal species].” Each diagonal line of points corresponds to different species in the same sample, and because community pathway richness is computed as the total number of pathways [across all species in the sample] minus the number of pathways in the focal species, the current Figure 5B is really plotting y against X-y for each sample (where X is a sample’s total community pathway richness, and y is the pathway richness of an individual species in that sample). This computation fails to account for the possibility that a pathway in an excluded focal species will still be present in the community due to redundancy, and indeed BQH tests for whether this redundancy is kept low in diverse communities due to mechanisms such as gene loss.

We attempted to instead plot community pathway richness defined as the number of unique pathways covered by all species other than the focal species. This is equivalent to [number of unique pathways across all species in a sample] minus the [number of pathways that are ONLY present in the focal species and not any other species in the sample]. However, when we recomputed community pathway richness this way, it is rare that a pathway is present in only one species in a sample. Moreover, we find that with the exception of E. coli, focal species pathway richness tended to be very similar across the 469 samples, often reaching an upper limit of focal species pathway richness observed. (It is unclear to what extent lower pathway richnesses are due to low species abundance/low sample coverage versus gene loss). This new plot reveals even more regularities and is difficult to interpret with respect to BQH. (Note that points are colored by species; the cluster of black dots with outlying high focal pathway richness corresponds to the “unclassified” stratum which can be considered a group of many different species.)

Overall, because community pathway richness (excluding a focal species) seems to primarily vary with sample rather than focal species in this dataset when using the most simple/strict definition of community pathway richness as described above, it is difficult to probe the Black Queen Hypothesis using a plot like Figure 5B. As pointed out by reviewers, lack of sequencing depth to analyze strain-level diversity and accurately quantify pathway abundance, irrespective of species abundance, seems to be a major barrier to this analysis. As such, we have decided to remove Figure 5B from the paper and rewrite some of our conclusions accordingly.

Finally, I also have some conceptual concerns regarding the genomic analysis. Namely, genes can be used for biosynthesis of e.g. building blocks, but also for consumption of nutrients. Under the Black Queen Hypothesis, we would expect the adaptive loss of biosynthetic genes, as those nutrients become provided by the community. However, for catabolic genes or pathways, I would expect the opposite pattern, i.e. the gain of catabolic genes that would allow taking advantage of a more rich environment resulting from a more diverse community (or at least, the absence of pathway loss). These two opposing forces for catabolic and biosynthetic genes/pathways might obscure the trends if all genes are pooled together for the analysis. I believe this can be easily checked with the data the authors already have, and could allow the authors to discuss more in detail the functional implications of the trends they see and possibly even make a stronger case for their claims.

We thank the reviewer for their suggestion. As explained above, we have removed the pathway analysis from the paper due to technical reasons. However, we did investigate catabolic and biosynthetic pathways separately as suggested by the reviewer as we describe below:

We obtained subsets of biosynthetic pathways and catabolic pathways by searching for keywords (such as “degradation” for catabolic) in the MetaCyc pathway database. After excluding the “unclassified” species stratum, we observe a total of 279 biosynthetic and 167 catabolic pathways present in the HMP1-2 pathway abundance dataset. Using the corrected definition of community pathway richness excluding a focal species, for each pathway type—either biosynthetic or catabolic—we plotted focal species pathway richness against community pathway richness including all pathways regardless of type:

We observe the same problem where, within a sample, community pathway richness excluding the focal species hardly varies no matter which focal species it is, due to nearly all of its detected pathways being present in at least one other species; this makes the plots difficult to interpret.

Reviewer #2 (Public Review):

The authors re-analysed two previously published metagenomic datasets to test how diversity at the community level is associated with diversity at the strain level in the human gut microbiota. The overall idea was to test if the observed patterns would be in agreement with the "diversity begets diversity" (DBD) model, which states that more diversity creates more niches and thereby promotes further increase of diversity (here measured at the strain-level). The authors have previously shown evidence for DBD in microbiomes using a similar approach but focusing on 16S rRNA level diversity (which does not provide strain-level insights) and on microbiomes from diverse environments.

One of the datasets analysed here is a subset of a cross-sectional cohort from the Human Microbiome Project. The other dataset comes from a single individual sampled longitudinally over 18 months. This second dataset allowed the authors to not only assess the links between different levels of diversity at single timepoints, but test if high diversity at a given timepoint is associated with increased strain-level diversity at future timepoints.

Understanding eco-evolutionary dynamics of diversity in natural microbial communities is an important question that remains challenging to address. The paper is well-written and the detailed description of the methodological approaches and statistical analyses is exemplary. Most of the analyses carried out in this study seem to be technically sound.

We thank the reviewer for their kind words, comments, and suggestions.

The major limitation of this study comes with the fact that only correlations are presented, some of which are rather weak, contrast each other, or are based on a small number of data points. In addition, finding that diversity at a given taxonomic rank is associated with diversity within a given taxon is a pattern that can be explained by many different underlying processes, e.g. species-area relationships, nutrient (diet) diversity, stressor diversity, immigration rate, and niche creation by other microbes (i.e. DBD). Without experiments, it remains vague if DBD is the underlying process that acts in these communities based on the observed patterns.

We thank the reviewer for their comments. First, regarding the issue of this being a correlative study, we now more clearly acknowledge that mechanistic studies (perhaps in experimental settings) are required to fully elucidate DBD and BQH dynamics. However, we note that our correlational study from natural communities is complementary to experimental and modeling studies, to test the extent to which their predictions hold in more complex, realistic settings. This is now mentioned throughout the manuscript, most explicitly at the end of the Introduction:

“Although such analyses of natural diversity cannot fully control for unmeasured confounding environmental factors, they are an important complement to controlled experimental and theoretical studies which lack real-world complexity.”

Second, to increase the number of data points analyzed in the Poyet study, we now include 15 species and four different hosts (new Figure 5). The association between community diversity and gene loss is now much more statistically robust, and consistent across the Poyet and HMP time series.

Third, we acknowledge more clearly in the Discussion that other processes, including diet and other environmental factors can generate the DBD pattern. We also now stress more prominently the possibility that strain migration across hosts may be responsible for the patterns observed. For example, in Figure 1, we illustrate the possibility of strain migration generating the patterns we observe.

Below we quote a paragraph that we have now added in the Discussion:

"Second, we cannot establish causal relationships without controlled experiments. We are therefore careful to conclude that positive diversity slopes are consistent with the predictions of DBD, and negative slopes with EC, but unmeasured environmental drivers could be at play. For example, increased dietary diversity could simultaneously select for higher community diversity and also higher intra-species diversity. In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

Finally, we now put more emphasis on the importance of migration (strain invasion) as a non-exclusive alternative to de novo mutation and gene gain/loss. This is mentioned in the Abstract and is also illustrated in the revised Figure 1.

Another limitation is that the total number of reads (5 mio for the longitudinal dataset and 20 mio for the cross-sectional dataset) is low for assessing strain-level diversity in complex communities such as the human gut microbiota. This is probably the reason why the authors only looked at one species with sufficient coverage in the longitudinal dataset.

Indeed, this is a caveat which means we can only consider sub-species diversity in relatively abundant species. Nevertheless, this allows us to study dozens of species in the HMP and 15 in the more frequent Poyet time series. As more deeply sequenced metagenomes become available, future studies will be able to access the rarer species to test whether the same patterns hold or not. This is now mentioned prominently as a caveat our study in the second Discussion paragraph:

“First, using metagenomic data from human microbiomes allowed us to study genetic diversity, but limited us to considering only relatively abundant species with genomes that were well-covered by short sequence reads. Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome. However, it is notable that the majority of the dozens of species across the two datasets analyzed support DBD, suggesting that the phenomenon may generalize.”

We also note that rarefaction was only applied to calculate community richness, not to estimate sub-species diversity. We apologize for this confusion, which is now clarified in the Methods as follows:

“SNV and gene content variation within a focal species were ascertained only from the full dataset and not the rarefied dataset.”

Analyzing the effect of diversity at a given timepoint on strain-level diversity at a later timepoint adds an important new dimension to this study which was not assessed in the previous study about the DBD in microbiomes by some of the authors. However, only a single species was analysed in the longitudinal dataset and comparisons of diversity were only done between two consecutive timepoints. This dataset could be further exploited to provide more insights into the prevailing patterns of diversity.

We thank the reviewer for raising this point. We now have considered all 15 species for which there was sufficient coverage from the Poyet dataset, which included four different stool donors. Additionally, in the HMP dataset, we analyze 54 species across 154 hosts, with both datasets showing the same correlation between community diversity and gene loss.

Additionally, we followed the suggestion of the reviewer of examining additional time lags, and in Figure 5 we do observe a dependency on time. This is now described in the Results as follows:

“Using the Poyet dataset, we asked whether community diversity in the gut microbiome at one time point could predict polymorphism change at a future time point by fitting GAMs with the change in polymorphism rate as a function of the interaction between community diversity at the first time point and the number of days between the two time points. Shannon diversity at the earlier time point was correlated with increases in polymorphism (consistent with DBD) up to ~150 days (~4.5 months) into the future (Figure S4), but this relationship became weaker and then inverted (consistent with EC) at longer time lags (Fig 5A, Table S8, GAM, P=0.023, Chi-square test). The diversity slope is approximately flat for time lags between four and six months, which could explain why no significant relationship was found in HMP, where samples were collected every ~6 months. No relationship was observed between community richness and changes in polymorphism (Table S8, GAM, P>0.05).”

Finally, the evidence that gene loss follows increase in diversity is weak, as very few genes were found to be lost between two consecutive timepoints, and the analysis is based on only a single species. Moreover, while positive correlation were found between overall community diversity and gene family diversity in single species, the opposite trend was observed when focusing on pathway diversity. A more detailed analysis (of e.g. the functions of the genes and pathways lost/gained) to explain these seemingly contrasting results and a more critical discussion of the limitations of this study would be desirable.

We agree that our previous analysis of one species in one host provided weak support for gene loss following increases in diversity. As described in the response above, we have now expanded this analysis to 15 focal species and 4 independent hosts with extensive time series. We now analyze this larger dataset and report the more statistically robust results as follows:

“We found that community Shannon diversity predicted future gene loss in a focal species, and this effect became stronger with longer time lags (Fig 5B, Table S9, GLMM, P=0.006, LRT for the effect of the interaction between the initial Shannon diversity and time lag on the number of genes lost). The model predicts that increasing Shannon diversity from its minimum to its maximum would result in the loss of 0.075 genes from a focal species after 250 days. In other words, about one of the 15 focal species considered would be expected to lose a gene in this time frame.

Higher Shannon diversity was also associated with fewer gene gains, and this relationship also became stronger over time (Fig 5C, Table S9, GLMM, P=1.11e-09, LRT). We found a similar relationship between community species richness and gene gains, although the relationship was slightly positive at shorter time lags (Fig 5D, Table S9, GLMM, P=3.41e-04, LRT). No significant relationship was observed between richness and gene loss (Table S9, GLMM, P>0.05). Taken together with the HMP results (Fig 4), these longer time series reveal how the sign of the diversity slope can vary over time and how community diversity is generally predictive of reduced focal species gene content.”

As described in detail in the response to Reviewer 1 above, we found that the HUMAnN2 pathway analyses previously described suffered from technical challenges and we deemed them inconclusive. We have therefore removed the pathway results from the manuscript.

Reviewer #3 (Public Review):

This work provides a series of tests of hypothesis, which are not mutually exclusive, on how genomic diversity is structured within human microbiomes and how community diversity may influence the evolution of a focal species.

Strengths:

The paper leverages on existing metagenomic data to look at many focal species at the same time to test for the importance of broad eco-evolutionary hypothesis, which is a novelty in the field.

Thank you for the succinct summary and recognition of the strengths of our work.

Weaknesses:

It is not very clear if the existing metagenomic data has sufficient power to test these models.

It is not clear, neither in the introduction nor in the analysis what precise mechanisms are expected to lead to DBD.

The conclusion that data support DBD appears to depend on which statistics to measure of community diversity are used. Also, performing a test to reject a null neutral model would have been welcome either in the results or in the discussion.

In our revised manuscript, we emphasize several caveats – including that we only have power to test these hypotheses in focal species with sufficient metagenomic coverage to measure sub-species diversity. We also describe more in the Introduction how the processes of competition and niche construction can lead to DBD. We also acknowledge that unmeasured abiotic drivers of both community diversity and sub-species diversity could also lead to the observed patterns. Throughout the manuscript, we attempt to describe the results and acknowledge multiple possible interpretations, including DBD and EC acting with different strengths on different species and time scales. Our previous manuscript assessing the evidence for DBD using 16S rRNA gene amplicon data from the Earth Microbiome Project (Madi et al., eLife 2020) assessed null models based on neutral ecological theory, and found it difficult to explain the observation of generally positive diversity slopes without invoking a non-neutral mechanism like DBD. While a new null model tailored to metagenomic data might provide additional nuance, we think developing one is beyond the scope of the manuscript – which is in the format of a short ‘Research Advance’ to expand on our previous eLife paper, and we expect that the general results of our previously reported null model provide a reasonable intuition for our new metagenomic analysis. This is now mentioned in the Discussion as follows:

“In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

Author Response

Reviewer #2 (Public Review):

1&2) Throughout the paper, the authors use a BiFC assay to monitor direct interactions between GDOWN1 and other transcription factors in the cell. While this assay works well for their experiments, we are unsure why GDOWN1 appears to interact with every protein found in the cytoplasm. This is particularly concerning when we look at GDOWN1 interacting with itself (Figure 1D), as GDOWN1 is not known to self-oligomerize. The authors should provide a negative control that GDOWN1 does not non-specifically interact with any cytoplasm-localized protein. Additionally, every GDOWN1 truncation tested was able to interact with NELF-E. We are unsure why each truncation tested (given that they tested multiple non-overlapping GDOWN1 regions) can interact with NELF-E. Do the authors believe that NELF-E directly interacts with every tested GDOWN1 construct? We believe that demonstration of BiFC specificity is critical for the conclusions drawn in the manuscript.

Thank you for your comments and valuable suggestions! We added more negative BiFC controls in the revised manuscript to demonstrate the specificity of BiFC assays (Figure 1——figure supplement 1D). Since both reviewers brought up this question, we provided our answers to this question above in the “Common concerns by the Reviewers” session (Q#1).

3) The authors note that the NES1 site is not as strong as the NES2 site at regulating exportin 1-dependent nuclear export. However, they suggest this is because mutating the NES2 site is more likely to disrupt the CAS site nearby. We ask the authors to expand on this concept. Do they have direct evidence that NES2 disrupts CAS activity (such as regulating its association with the nuclear pore complex)?

From Figure 4A, we can see that both NES1 (4A-b) and NES2 (4A-d) work as functional nuclear export signals. When NES1 was mutated (4A-c), NES2 and CAS both remained functional in blocking GDOWN1’s nuclear shuttling upon LMB addition. However, when NES2 was mutated (4A-e), comparing the localization changes before and after LMB addition, we concluded that NES1 remained functional, while the cytoplasmic retention activity of CAS was partially lost. From the quantification of the images, it seems that NES1 has a stronger activity than NES2 in terms of the LMB responsiveness/CRM1-depentent nuclear export activity, while apparently NES2 exhibits another layer of regulation/correlation on the CAS activity.

To further confirm this observation, we generated a HeLa stably cell line expressing GDOWN1(NES2 mutant)-Venus and tested the subcellular localization of this mutant. As shown in the Figure 4C of the revised manuscript, compared with the wild type GDOWN1, loss of the NES2 activity directly caused the loss of the perinuclear staining, which was consistent to the defect of the CAS mutant. These results further support that the mutagenesis of NES2 disrupts the CAS-mediated association to the nuclear pore complex.

4) The authors show the critical role of the NES1, NES2, and CAS sites for the localization and function of GDOWN1. Have the authors checked post-translational modification databases to check if any of the identified sites could be post-translationally modified and thereby regulated? Elucidation of the mechanism by which GDOWN1 localization is regulated is of broad interest to the transcription community.

Good suggestion! It is worthy of checking and testing the potential modifications on the key arginines identified in CAS (R352, R354, and R357). We did check the web tools for arginine methylation site prediction (http://msp.biocuckoo.org/online.php), but none pf the known motifs was found to match with the CAS sequences of GDOWN1. In addition, our pilot studies for the treatments using the inhibitors of arginine methyltransferases (- or + LMB) did not result in any nuclear accumulation of GDOWN1 (data not shown). So far, we do not have any strong evidence to confirm that these arginines are directly modified in our assays, and we cannot exclude the possibilities of other amino acids nearby also play key roles on the CAS function. Thus, more research is badly needed to uncover the regulatory mechanism of CAS.

Author Response

Reviewer #1 (Public Review):

This study aimed to test the hypothesis that resident immune cells are strategically positioned along the epididymal duct to provide different immunological environments to prevent pathogens from ascending the urogenital tract. By using an epididymitis mouse model, the differential responses at different segments along the epididymis were examined at both histological and gene expression levels, and the data appeared to support their hypothesis. Furthermore, single-cell RNA-seq analyses identified the composition of resident immune cell types along the epididymal duct, and the parabiosis model further corroborated the major findings. Overall, the study was well conducted and the major conclusion seems well supported. The only caveat is the lack of elucidation on the direct or indirect impact of the resident immune cells on sperm maturation.

We thank the reviewer for his/her feedback and the valuable comments.

We are aware of the fact that the current manuscript lacks further experimental evidence on the effects of immune cells on organ function, especially sperm maturation, and agree that this would constitute a relevant object to study. Although the assessment of the direct or indirect impact of particular immune cells on sperm maturation would require further intensive research, encompassing e.g. the consequences of targeted cell depletions (using several transgenic mouse models) with comprehensive follow-up analysis (i.e. by detecting anti-sperm antibodies, assessing the potential appearance of sperm-induced autoimmune reactions in vivo and conducting in vitro co-culture assays besides conducting sperm functional tests to evaluate capacitation and fertilization competencies). A study of this magnitude is outside of the scope of the present manuscript and would form a separate examination that alone would take more than a year to perform. Therefore, our intention was to submit this article as a ‘Tools and Resource’ article as it is providing a detailed overview of all immune cell types that are shaping the regional immunological landscape based on crucial information about their transcriptional profiles on single cell resolution. In our view the provided data are closing a gap in the current state of knowledge (particularly regarding the transcriptional identity and distribution of described immune cell populations) and will serve as a relevant common platform for current and future approaches.

Reviewer #2 (Public Review):

Pleuger et al. investigated the heterogeneity of resident immune cells in the murine epididymis. The response of immune cells in the different epididymal segments was characterized following acute bacterial infection by flow cytometry, and immunofluorescence microscopy. Single-cell RNA sequencing analysis and parabiosis experiments were performed to provide an atlas of resident immune cells and their etiology in the epididymis under steady-state conditions. The authors conclude that distinct immune cell phenotypes govern specific responses of the different epididymal segments during acute bacterial infection. Overall, the conclusions of this study are well supported by the data, but some specific aspects related to the region-specific phenotypes of resident immune cells need to be revisited.

1) In order to conclude that there was an infiltration of neutrophils and monocytes following bacterial injection, the authors should provide flow cytometry quantification of the percentages of immune cell subsets relative to live cells, rather than relative to the CD45+ population.

Following the reviewer’s request, we have replaced the data previously shown in figure 2 by a completely new high-dimensional flow cytometry analysis including FltSNE visualization of CD45+ cell populations in different epididymal regions (IS, Caput, Corpus, Cauda) under different conditions (naive, sham, UPEC 10 days post infection). In addition, we have included bar diagrams displaying the percentage of all investigated immune cell subsets in relation to single live cells. The results displayed in the new figure are similar to previous shown data, but the overall figure layout and visualization method is clearer and more comprehensible. We thank the reviewer for the helpful comment.

2) In general, all flow cytometry and immunofluorescence data should be presented and discussed with respect to previously published studies.

This is reflected in the discussion (line 564-575) and in addition by addressing similar points raised by the reviewers.

3) A surprisingly low number of CX3CR1-EGFP cells was detected by immunofluorescence in the cauda. This is not in agreement with previous studies showing a similar % of CX3CR1-EGFP cells in the IS and cauda regions by immunofluorescence and flow cytometry. The authors need to discuss this discrepancy. Perhaps the different fixation procedures used in the current study compared to those used in previous studies could account for the loss of EGFP in epididymis cryo-sections. As such, cells that appear to be F4/80 positive but negative for EGFP by immunofluorescence might simply be due to the loss of cytoplasmic EGFP, while F4/80 immunogenicity remained intact.

Within our study, we have shown by combining scRNASeq, flow cytometry and immunostaining that distinct macrophage subgroups co-exist within the epididymis and that the diversity increases towards the cauda. Based on these data, we can assume that cells that appear to be F4/80 positive but negative for CX3CR1 (e.g. clusters 6-9 of the macrophage clustering show a very low level or even lack of Cx3cr1 expression) are distinct from CX3CR1+F4/80+ cells (e.g. clusters 1 and 2 of the macrophage subclustering, both showing a high expression of Cx3cr1). Therefore, our immunostaining (on Cx3cr1GFPCcr2RFP reporter mice) and flow cytometry data (on wild type C57BL/6J mice) in Figure 6 are in line with our transcriptomic data and strongly support the co-existence of both populations. We have seen the described gradient of macrophage numbers (decreasing from IS towards cauda) in all independently performed experiments (naive control group in infection experiments, steady-state characterization in wild type and transgenic mice). A previous study, however, demonstrated a constant CX3CR1+ cell ‘number’ throughout all epididymal regions (~5-6% in live cells, (Battistone et al., 2020)). Here, indeed we notice a discrepancy to our results that show a relatively high ‘number’ of CX3CR1+ cells in the initial segment of naive mice (20% in single live cells, new Figure 2G) that decreases towards the cauda (~5% in single live cells, data shown in the new Figure 2 of naive mice). [It needs to be mentioned that these numbers are slightly different to the percentage of CD45+ cells in single live cells shown in Figure 4 due to different settings in the flow cytometry (thresholding to exclude spermatozoa and debris)]. However, another study (Voisin et al., 2018) showed a comparable ratio of total macrophages within caput and cauda with a similar gradient throughout the epididymal regions (significantly lower ratio within the cauda compared to the caput). Although this study discriminated only between caput and cauda, these data are in line with our results.

Nevertheless, it needs to be noted that calculating the percentage of a population in single live cells is not representing an unbiased quantification approach as this calculation is highly dependent on previous gating (thresholding, aimed events, single cells as well as live cells; the latter is, in turn, dependent on the experimental procedures that may have an impact on the cell viability and antigen recognizability, see below). Rather, it provides important information about the population distribution among regions or conditions. For this reason, a comparison among studies as requested above is not expedient from our point of view. This as well as other studies are limited in the way that they lack an absolute quantification of immune cell populations as that would require e.g. a prior cell-counting or the relation of absolute cell numbers to mg of tissue as conducted in the parabiosis experiment shown in Figure 7 (that in turn is also limited for the epididymal regions due to the necessity of pooling tissue from several mice to obtain a sufficient cell number and thus, masking individual differences). Another alternative would be quantitative morphometric analysis of stained sections that has not been performed in the present study.

By comparing the protocol for the cell isolation and preparation of the single cell suspension between our study and previous reports (Battistone et al., 2020), it appears that different protocols have been applied that indeed could have a major impact. In this regard, the study of (Battistone et al., 2020) used a mixture of collagenase type I (0.5 mg/ml) and collagenase type II (0.5 mg/ml) and incubated tissue fragments for a short period (30 minutes) at 37°C. In contrast, in this study we have chopped the tissue fragments with scissors until no fragments were visible anymore then followed by enzymatic digestion (shaking at 37°C for 45 minutes with 1.5 mg/ml collagenase type IV and 60 U/ ml DNAse). Afterwards, we aspirated the digest 5-6 times through a 30G needle (to release pre-digested sticky cells from each other by shear forces) before passing through a 70 µm cell strainer. We have experienced that we can significantly increase the number of viable cells when using collagenase type IV for a longer time at the ideal concentration at 1.5 mg/ml (similar concentration and incubation duration with collagenase I resulted in a higher proportion of dead cells in the analysis). A longer incubation time increases the obtained cell numbers especially from the IS where the epithelial cells are densely connected to each other. In general, collagenase type IV has a lower tryptic activity than other collagenases and therefore, the usage of collagenase IV limits the damage on membrane proteins and receptors (an overview of the different collagenase types with respective references can be found at: https://www.worthington-biochem.com/products/collagenase/manual).

In summation, we agree with the reviewer that very likely methodological differences account for the mentioned discrepancy of our data to Battistone et al (2020) and raised this point in the revised discussion(ses line 559-564).

The statement "Intriguingly, our data revealed that distinct immunological landscapes exist within proximal (IS, caput) and distal regions (corpus, cauda), that are tailored to the respective needs of the microenvironments" implies that this is the first study that describes immune cell heterogeneity in the epididymis. Please rephrase this statement as previous studies have already shown the segment-specific heterogeneity of resident immune cells in this organ.

To address the reviewer's comment, we have rephrased the statement to “our data unraveled the transcriptional identity and tissue location of extravascular immune cells and further support the existence of distinct immunological environments along the epididymal duct that are tailored to the respective needs of the microenvironment” within the discussion section (line 555-558). Moreover, the previous investigations on epididymal immune cells were acknowledged and cited within the introduction (line 107-124) as well as in the discussion (line 549-554, line 564-575, line 580-584,). We hope that this satisfactorily addresses the reviewer’s critique.

The conclusion that macrophages constitute the major immune cell population of the murine epididymis is not supported by the data provided here. In fact, the authors found that macrophages account for only approximately 20% of CD45+ immune cells in the cauda. The authors should, therefore, modify their conclusion to state that macrophages constitute the major immune cell population in the IS. In fact, this conclusion would be more in line with previously published studies.

The reviewer is correct and we have changed the conclusion to “macrophages constitute the major immune cell population, especially within the IS” accordingly (see line 559-560).

The authors conclude that fewer intraepithelial CX3CR1-EGFP+ cells are present in the cauda, but they do not explain how they actually quantified these intraepithelial cells. A description of how these results were obtained is missing.

We agree with the reviewer that we did not quantify cells based on our immunostaining. All quantification approaches were obtained by flow cytometry on wild type mice with respective surface staining (acc. to previous selection of markers derived from scRNASeq, see Figure 6) and show only ratios, but no absolute numbers. An additional counting of the immunostained section would be required to ultimately determine whether these cells are quantitatively different in the cauda compared to the IS. The respective sentence, however, does not intend to compare the abundance of these cells among epididymal regions, rather it is stating that ‘the distal regions are populated by a more heterogeneous macrophage pool consisting of less intraepithelial CX3CR1+ macrophages, but higher abundance of interstitial pro-inflammatory monocyte-derived CCR2+MHC-II+, vasculature-associated TLF+ macrophages as well as CX3CR1-TLF-CCR2- macrophages’. This statement is pointing to the increasing macrophage heterogeneity towards the distal parts and is based on the clustering of the scRNASeq data, flow cytometry analysis and supported by the immunostaining that localized these populations in the epididymal compartments. For this reason flow cytometry and immunostaining are combined included in Figure 6 to display the ratio of identified macrophage subgroups to each other (Fig. 6B, bar diagram showing % of distinct subpopulations in total F4/80+ cells) with supportiving immunostaining using the same marker for localization.

Author Response

Reviewer #3 (Public Review):

Weaknesses

The spontaneous activity of the network is extremely low, with [0.02 0.09] spks/s considered as a high activity range. Granted, this is based on ex vivo measurements. However, if this phenomenon is to be considered computationally relevant, as the authors claim, the paper should have examined the reliability of propagation and routing with in vivo activity levels.

The above weakness is a special case of the issue that the limits of applicability/robustness of results to model assumptions have not been well established. In particular, it is not clear how strong the strongest weights must be whilst still enabling long sequences, and what is the dependence of the results on the parameters of the distance-dependent connectivity.

Regarding the two first weaknesses listed in Reviewer #3 Public Review, we wish to note that:

● The statement that our estimate of spontaneous activity “is based on ex vivo measurements” is incorrect. Our single-cell and connectivity parameters are certainly based on ex vivo measurements, but the range of spontaneous activity that the Reviewer cites ([0.02 0.09] spks/s) is an estimate from in vivo recordings. Furthermore, in our model, we explored mean firing rates higher than this in vivo range and still observed sequences.

● While the Reviewer states that “it is not clear how strong the strongest weights must be”, we do provide a lower-bound estimate. We explored simulations where we truncated sections of the distribution of synaptic strengths and observed that networks that included the bottom 90% of connections did not produce sequences.

Author Response

Reviewer #1 (Public Review):

This study sets out to decipher whether the eDNA that promotes biofilm dispersal in Caulobacter crescentus biofilms is released when a random portion of cells lyse within biofilms, or whether eDNA release is a regulated process. They start by investigating whether any of the C. crescentus TA systems contribute to biofilm-associated cell death, and find that one of the systems, ParDE4 is responsible for cell death and eDNA release. They go on to show that this system is O2-regulated and thus contributes to cell death in particular in the oxygen limited interior regions of biofilms. These findings contribute significantly to our understanding of the biological functions of toxin-antitoxin systems, mechanisms of bacterial programmed cell death, and biofilm growth. The notion that TA systems function in cell death in particular has been controversial, and often based on overexpression of the toxin component, therefore the fact that this study uses a TA system in its native genomic context is notable. The authors also show clearly the somewhat counterintuitive result that the cell death (and presumably, toxin activity) is negatively correlated with transcription of the TA system. This is consistent with what is known about TA biology (but not with many past TA papers, which often correlated TA transcription with toxin activation). The study also provides a logical rationale for how ParDE4 mediated cell death ultimately contributes to bacterial fitness. The paper is well written and figures are clear and easy to follow.

There are two relatively minor shortcomings of the paper, both acknowledged as caveats by the authors in their discussion. First, while the authors do include one experiment that addresses whether the toxin is responsible for the cell death (Fig 3), they do not show direct evidence of the activity of the toxin other than cell death/eDNA release. Second, the authors do not address whether the reduced TA transcription they observe is what causes the release of the toxin and thus the cell death phenotype. This seems likely to be the case based on previous studies of other TA systems (e.g. TA systems involved in plasmid segregation, most clearly shown for CcdAB, or more recently the ToxIN system during phage infection). Connecting this directly would be a very valuable addition to this study.

We thank the reviewer for those positive comments. We agree that the TA system we describe in this study needs to be characterized in more detail. Understanding how this TA expression levels are linked to cell death is our next goal and will be the scope of a future publication.

We now discuss the important missing point about possible TA expression being linked to cell death and refer to CcdAB, ToxIN and other relevant systems, as well characterized examples of such mechanisms. In the introduction, we now present the role of TAS in plasmid addiction and phage defense mechanisms. We also provide more information about those systems in the discussion and speculate the similarities with the TAS described here (see our reply to essential revisions above).

Reviewer #2 (Public Review):

In this work, the authors present compelling evidence that a toxin-antitoxin system contributes to biofilm dispersal under oxygen limited conditions. This work makes important contributions to two areas of microbial physiology; functional understanding of toxin-antitoxin systems, which have remained largely elusive, and mechanistic regulation or biofilm dispersal, is a critical, but less understood aspect of biofilm physiology.

A major goal of the work described in this manuscript was to better understand the regulation of biofilm dispersal. These authors provide compelling evidence that the parDE4 toxin-antitoxin (TA) system in Caulobacter crescentus mediates enhanced cell death under conditions of oxygen limitation. This group previously reported that extracellular DNA (eDNA) inhibits attachment of new-born swarmer cells. Here they build on that observation by identifying a genetic module that contributes to cell death and DNA release under oxygen limitation, a sub-optimal condition present in a dense biofilm community, and demonstrate that parDE4 affects biofilm development. Together, this work makes important contributions toward understanding functional roles for toxin-antitoxin systems and regulation of mature stages of biofilm development. In addition, although eDNA is often depicted as having a structural role in strengthening and maintaining biofilms in some species, this work further establishes that eDNA can have multiple roles in biofilms including contributing to dispersal in Caulobacter.

Strengths of this work include 1) comprehensive evaluation of multiple paralogous TAS and specific identification of the contribution of parDE4 to cell death, eDNA release and biofilm restriction, 2) genetic dissection of the TA pair to establish that the ParD4-antitoxin prevents eDNA release and promotes biofilm formation in a ParE4-toxin dependent manner, 3) provision of evidence that the parDE system affects cell death / eDNA release, but not responsiveness to eDNA, 4) demonstration of an anti-correlation between expression of parDE and ccoN, a hypoxic responsive gene, at both the population level under different growth conditions and at the single cell level within different growth conditions.

We thank the reviewer for these positive comments.

One weakness of this work is that the authors do not directly measure O2 concentrations in their growth conditions. However, they do monitor activity of an established hypoxic responsive promoter, which provides strong evidence that the various conditions tested do indeed affect oxygen concentrations in the culture medium. Nevertheless, it is difficult to assess oxygen availability in the flow cell experiments, which will be dependent on both dissolved oxygen in the media pumped through the flow cell and cell density within the flow cells. In the competition experiments, the ∆parDE4 mutant has an advantage before there seems to be an appreciable cell density, perhaps reflecting low oxygen in the growth medium or a monolayer of cells that is not obvious in the images as presented. It would be interesting to evaluate expression of ccoN in biofilms grown under these flow conditions.

We agree with the reviewer that one limitation of our study is that we could not directly measure the O2 concentration in our different growth conditions. Unfortunately, we were unable to find a way to reliably and reproducibly assay the dissolved O2 concentration in our experimental set-ups (both static biofilms and flow-cells). We think that regulation of parDE4 expression is linked to the composition of the local environment surrounding each cell, and offering a proxy via ccoN expression is the best method we could provide to assess this. Results provided in Figures 7 and S3 (now S5) clearly show that cells that respond to limiting O2 levels (by activating ccoN expression) have low parDE4 expression. We also show in this set of experiments that, at the population level, there are cells highly expressing ccoN or parDE4 regardless of the culture conditions and the overall O2 levels.

We now provide the expression of ccoN in different areas of biofilms, in addition to the already presented parDE4 expression, in Fig. 8A. We quantified ccoN transcription levels using the PccoN-lacZ construct (already used to generate data in Figure 5) and the fluorogenic ß-galactosidase substrate we used to quantify parDE4 expression in biofilms in the first version of this manuscript (Figure 8A). These new results now show that in biofilm areas where parDE4 is more expressed, ccoN expression is low and vice-versa and confirm other observations made throughout this work.

The discussion regarding the observation that parDE expression drops under activating (oxygen limiting) conditions is contradictory to what I would expect based on the early findings about TA systems as genetic stabilization systems. The authors seem to expect that conditions that activate the toxin should correspond to increase expression of the TA operon. However, TA systems have frequently been characterized as DNA stabilization systems for plasmids or other mobile elements because the toxin proteins are more stable than the antitoxin proteins. In these cases, if the gene pair is lost (or in this case if expression is decreased) then the toxin protein persists longer than the antitoxin protein, effectively activating the toxin to arrest or kill cells that have lost (or in this case turned off) the gene pair. Thus I disagree with the statement that this is a "novel regulatory mechanism of PCD that remains to be understood" (line 436-7).

The sentence preceding this one was "We are unaware of cases where reduced TAS expression is correlated with the condition that activates the PCD in biofilm regulation." and we suggested a "novel regulatory mechanism of PCD" in the context of biofilm formation. However, we realize now that our statements could be misleading and we entirely rewrote this section (Lines 510-519: " It is interesting to note that the "neutralized" steady state of the ParDE4 TAS, when the toxin is inactivated, seems to be when O2 is abundant, i.e, when parDE4 transcription is at its highest. In most studied TAS, stresses have been shown to induce transcription of TAS (LeRoux et al., 2020, Jurėnas et al., 2022), but here, the stress inflicted on the cells by O2 limitation is accompanied by a lower expression of parDE4. We are unaware of cases where reduced TAS expression is correlated with the condition that activates the PCD in biofilm regulation. This suggests a novel regulatory mechanism of PCD, in the context of biofilms, that remains to be understood.").

Differential stability of toxin and antitoxin proteins provides a reasonable regulatory mechanism to explain the programed cell death observed. Testing of this, or other, mechanistic model(s) will be important in future studies of this system.

We agree with the reviewer and testing protein stability is definitively on the list of experiments to do to dissect this TA killing mechanism in the near future. As mentioned above, we have been unable to obtain antibodies to these proteins so far, delaying these types of experiments.

Author Response

Reviewer #1 (Public Review):

This paper proposes a 2D U-Net with attention and adaptive batchnorm modules to perform brain extraction that generalises across species. Generalisation is supported by a semi-supervised learning strategy that leverages test-time monte-carlo uncertainty to integrate the best-predicated labels into the training strategy. Monte-Carlo dropout maps also tend to align with inter-rate disagreement from manual segmentations meaning that they can realistically be used for fast QC. The networks (trained on a range of source domains) have been made publicly available, meaning that it should be relatively simple for users to apply them to their own cohorts, allowing for retraining on a very small number of labelled datasets. Overall the paper is exceptionally well written and validated, and the tool has broad application.

We thank this reviewer very much for these encouraging and valuable comments.

Reviewer #2 (Public Review):

In this manuscript, the authors are proposing a generalizable solution to masking brains from medical images from multiple species. This is done via a deep learning architecture, where the key innovation is to incorporate domain transfer techniques that should allow the trained networks to work out of the box on new data or, more likely, need only a limited training set of a few segmented brains in order to become successful.

The authors show applications of their algorithm to mice, rats, marmosets, and humans. In all cases, they were able to obtain high Dice scores (>0.95) with only a very small number of labelled datasets. Moreover, being deep-learning-based segmentation once a network has been trained is very fast.

The promise of this work is twofold: to allow for the easy creation of brain masking pipelines in species or modalities where no such algorithms exist, and secondly to provide higher accuracy or robustness of brain masking compared to existing methods.

I believe that the authors overstate the importance of generalizability somewhat, as masking brains is something that we can by and large do well across multiple species. This often uses specialized tools for human brains that the authors acknowledge work well, and in the usually simpler non-human (i.e. lissencephalic rodent) brains also work well using image registration or multi-atlas segmentation style techniques. So generalizability adds definite convenience but is not a game-changer.

The key to the proposed algorithm is thus that it works better than, or at least as well as, existing tools. The authors show multiple convincing examples that this is the case even after retraining with only a few samples. Yet in those examples, the authors proposed retraining the network on even subtle acquisition changes, such as moving in field strength from 7 to 9.4T. I tried it on some T2 weighted ex-vivo and T1 weighted manganese enhanced in-vivo mouse data and found that the trained brain extraction net does not generalize well. None of the pre-trained networks provided by the authors produced reasonable masks on my data. Using their domain adaptation retraining algorithm on ~20 brains each resulted in, as promised, excellent brain segmentations. Yet even subtle changes to out-of-sample inputs degraded performance significantly. For example, one set of data with a slight intensity drop-off due to a misplaced sat band created masks that incorrectly excluded those lower intensity voxels. Similarly, training on normal brains and applying the trained algorithm to brains with stroke-induced lesions caused the lesions to be incorrectly masked. BEN thus seems to be in need of regular retraining to very precisely matched inputs. In both those examples, the usual image registration/multi-atlas segmentation approach we use for brain masking worked without needing any adaptation.

Overall, this paper is filled with excellent ideas for a generalized brain extraction deep learning algorithm that features domain adaptation to allow easy retraining to meet different inputs, be they species or sequence types. The authors are to be highly commended for their work. Yet it appears to at the moment produce overtrained networks that are challenged by even subtle shifts in inputs, something I believe needs to be addressed for BEN to truly meet its promised potential.

We sincerely thank the reviewer for these constructive comments. We appreciate that the article is considered to be a valuable contribution to the field of neuroimaging by providing BEN as an efficient and generalisable deep learning based tool for brain extraction. The major concern of this Reviewer is that a pretrained BEN leads to unsatisfactory performance on some external data (e.g. the reviewer’s own data), although the domain adaptation retraining algorithm on ~20 brains did lead to, as promised, excellent segmentation results. Here, we would like to emphasize that the initial version of BEN on Github was designed to reproduce the results we presented in the manuscript, not an optimized version for processing external datasets. To address this issue, we have optimized the BEN pipeline in the revised version, which is summarized as follows:

1) Orientation detection. We found that in the original version of BEN, our training rodent images for BEN are all axial views, so it works the best on testing images of axial view. Therefore, if rodent MR images are loaded in other views (such as sagittal, coronal), the performance of BEN will degrade. To solve this issue, we have updated an orientation detection function in the BEN pipeline and automatically align other orientations to axial view, thus optimizing BEN’s performance.

2) Performance optimization using plug-and-play functions. We have added post-processing steps to improve performance and running logs for quick inspection.

3) Validation and tutorials. To further validate BEN’s generalization, we have evaluated BEN on two new external public ex-vivo MRI datasets (rTg4510 mouse: 25 ex-vivo scans, and C57BL/6 mouse: 15 ex-vivo scans). When only one label is used for BEN adaptation/retraining, impressive performance is achieved on both datasets, despite the fact that BEN was originally designed for in-vivo MRI data. To make the implementation transparent and give detailed guidance to users, we have prepared video tutorials on our Github/Documentation (https://github.com/yu02019/BEN#video-tutorials). Note that BEN’s performance may degenerate when dealing with MR images with low image quality. As an open-resource tool, BEN is extensible, our team will continuously maintain and update it.

Nevertheless, there could be a couple of reasons that cause suboptimal performance when using a pretrained BEN. We discuss them below and have revised the manuscript accordingly (last paragraph in Discussion).

On the one hand, as pointed out by the reviewer, domain generalization is a challenging task for deep learning. Although BEN could adapt to new out-of-domain images without labels (zero-shot learning) when the domain shift is relatively small (e.g. successful transfer between modalities and scanners with different MR strengths), the domain gap exists in ex-vivo MRI data used by the reviewer and in-vivo images in our training images could be so large that it compromises the performance. In this case, additional labeled data and retraining are indeed necessary for BEN to perform few-shot learning, which we have emphasized and demonstrated in our manuscript and confirmed by the reviewer (although in our opinion, it is possible we only need <5 more brains instead of 20 to complete the task).

On the other hand, as a deep learning tool, it is difficult or nearly impossible to guarantee optimal performance on any unseen data. This is also a motivation for us to design BEN as an extensible tool. As stated in the manuscript, the source domain for BEN is flexible and does not bind to Mouse-T2-11.7T, in our manuscript. Instead, users can provide their own data and pretrained network as a new source domain, therefore facilitating domain generalization by reducing the domain gap between the new source and target domains.

eLife assessment

This paper will be of interest to those studying DNA replication in the context of chromatin and development. This important study uncovers a new interaction partner for the chromatin protein SuUR and tries to understand how this complex (SUMM4) functions to control under-replication in polytene chromosomes. While the experiments are of high quality and carefully controlled, the data currently do not fully support all the conclusions, particularly as they relate to conclusions about DNA replication timing.

We appreciate a positive evaluation of our work. We agree that the relevance of under-replication phenomenon to the establishment of late replication in dividing cells has only been established based on circumstantial evidence. In the revised manuscript, we expand the explanation of this relationship and discuss limitations of the endoreplication model as applied to understanding of late DNA replication in the cell cycle of diploid cells. We also edited the abstract to soften our conclusions. We believe that the improvements made in the revised manuscript produced a more stringent alignment between our data and the conclusions.

Reviewer #1 (Public Review):

Andreyeva et al. developed a novel purification/mass spec approach to identify SuUR-associated proteins. From this biochemical tour de force, they identify a complex consisting of the insulator-associated protein Mod(Mdg4) and SuUR that they term, SUMM4. They show that this complex (at least SuUR) has ATPase activity, which is an exciting result was no known biochemical activity associated with SuUR. Given SuUR's function in the under-replication of Drosophila salivary glands, the authors show that SuUR and Mod(Mdg4) at least partially localize on polytene chromosomes and that SuUR displays at least a partial dependence on Mod(Mdg4) for localization to IH, but not PH regions. Finally, using two independent genetic reporters, they show that SuUR itself has an insulator function, which is a new function for SuUR and exciting as it is likely a diploid cell-specific function for SuUR. The authors then attempt to show the Mod(Mdg4) functions in under-replication. Unfortunately, under-replication is minimally, if at all, changed in the Mod(Mdg4) mutant. While the authors bring up several possible scenarios of why this could be, it is still uncertain whether Mod(Mdg4) has a direct effect on under-replication.

Strengths:<br /> The authors developed a very useful strategy to identify protein interactions through multiple purification steps using mass spectrometry. This approach can be applied to different systems and will be generally useful to the community. Through this approach, they provide very compelling data that SuUR and Mod(Mdg4) form a complex. Furthermore, the experiments all have been rigorously performed and the data is of high quality.

Weaknesses:<br /> The way the paper is written, its main focus is on under-replication. What the authors were not able to conclusively demonstrate is whether Mod(Mdg4) functions in under-replication.

We thank the Reviewer for a positive evaluation of our work, specifically the biochemical and cytological results. Unfortunately, this Reviewer was less convinced by our conclusions about the role of Mod(Mdg4) in regulation of under-replication. However, we believe that our data strongly implicate Mod(Mdg4) in under-replication:

1) Although SuUR is considered a bona fide suppressor of under-replication, its mutation does not fully restore DNA copy numbers in under-replicated regions of polytene chromosomes but, rather, by ~78% on average (Table 1). Although the mutation of mod(mdg4) produces a weaker recovery (~26% on average, Table 1), it is still robust and statistically significant. Presently, there is only one other mutant (Rif1) known to restore DNA copy numbers at most under-replicated regions in salivary gland polytene chromosomes.

2) DNA copy numbers in SuUR and Rif1 mutants, which are homozygous viable and fertile, are measured in L3 larvae produced from crosses of homozygous parents, i.e. in the absence of maternally contributed gene products. In contrast, mod(mdg4) is essential for viability, and the DNA copy numbers have to be measured in homozygotes that have Mod(Mdg4) protein and RNA loaded by heterozygous mothers. Since endoreplication initiates before the maternal product is exhausted, it limits the observed suppression. However, when we directly compare zygotic functions of SuUR and mod(mdg4) by analyzing the progeny of heterozygous mod(mdg4)/+ and SuUR/+ parents, they appear indistinguishable.

3) Finally, we demonstrate that Mod(Mdg4) is essential for the proper loading of SUUR in polytene chromosomes, thus implicating it as a direct, SUUR-dependent effector of late DNA replication.

In the revised manuscript, we provide a clearer explanation of our results. We hope that our arguments and modifications of the manuscript will alleviate the Reviewer’s concerns.

Reviewer #2 (Public Review):

This paper from the Fyodorov lab reports the isolation of a native protein complex of SUUR, a Drosophila SNF2-related factor, in a complex with Mdg4, an established chromatin boundary protein. The discovery of this native complex, called SUMM4, was enabled by the development of a mass spec-linked proteomic analysis of fractions from an unbiased, conventional multi-step chromatographic purification of low-abundance protein complexes. The authors validate the native interactions by co-immunoprecipitation and show further with recombinant proteins that SUUR displays ATPase activity, a property not previously shown, and which is stimulated by Mdg4. From a functional perspective, authors demonstrate that both components SUUR and Mdg4 mediate activities of the Drosophila gypsy insulator that blocks enhancer-promoter interactions and acts as a heterochromatin-euchromatin barrier, and moreover, has a role in the under-replication of intercalary heterochromatin.

Overall, this work is a substantial contribution to the field in two respects. First, it provides a new approach to the identification of novel native complexes that are of low abundance and difficult to isolate and identify by conventional biochemistry and mass spectrometry. Second, the interaction between Mdg4 and SUUR is novel and offers an ATP-driven pathway to be further investigated for understanding the mechanism of insulator (gypsy) function. Together, these advances are supported by the compelling quality and quantity of data. However, the paper does not read smoothly and can benefit from rewriting for readers who are not familiar with mass-spec proteomics or Drosophila biology.

We thank the Reviewer for a positive evaluation of our work. To improve clarity, we made several modifications of our manuscript as requested by the Reviewer.

Author Response

Reviewer #1 (Public Review):

The layered costs and benefits of translational redundancy by Raval et al. aim to investigate the impact of gene copy number redundancy on E. coli fitness, using growth rate in different media as the primary fitness readout. Genes for most tRNAs and the three ribosomal RNAs are present in multiple copies on the E. coli chromosome. The authors ask how alterations in the gene copy number affect the growth rate of E. coli in growth media that support different rates of growth for the wild type.

While it was shown before that mutants with reduced numbers of ribosomal RNA operons grow at reduced rates in rich medium (LB), this study extends these findings and reaches some important conclusions:

1) In a poor medium (supporting slow growth rates), the mutants with fewer rRNA operons actually grow faster than the wild type, showing that redundancy comes at a cost.

2) The same is true for mutants with reduced gene copy number of certain tRNAs and correlates with slower rates of protein synthesis in these mutants.

3) That rRNA operon gene copy number is more decisive for growth rate than any tRNA gene copy number (>1).

In addition, measurements of strains with deletions of genes encoding tRNA-modification enzymes that affect tRNA specificity are included. While interesting, no unifying conclusion could be reached on the impact of these mutations on growth rate.

Thank you for this clear summary of our work.

The well-known "growth law" relationships between growth rate and macromolecular composition (RNA/protein ratio, for example) specifically concern steady-state growth rates. It is concerning that all growth rates in this work were measured on cultures that were only back-diluted 1:100 from overnight LB precultures. That only allows 6-7 doubling times before the preculture OD is reached again. The exponential part of growth would end before that, allowing perhaps only 3-4 generations of growth in the new medium before the growth rate was measured. Thus, the cultures were not in balanced growth ("steady state") when the measurements were made, rather they were presumably in various states of adapting to altered nutrient availability.

A detailed connection with exact growth rate laws indeed requires growth rate measurement in steady-state. Hence, we refrained from making such a connection in this manuscript, though it would be an interesting future avenue to explore. Our main goal here was to ask how E. coli growth rate is affected by external nutrient availability and internal translation components. For this, the key comparisons involve the WT vs. gene deletion mutations, and rich vs. poor growth media. For any given comparison, strains were tested under identical conditions and experimental protocols, and hence we can address our main questions without the need to obtain steady-state growth. As an aside, we note that the nutrient fluctuations inherent in such experiments may also be more relevant than steady-state growth for natural bacterial populations.

As noted by the reviewer, we measured fitness only in a relatively narrow growth regime of several doublings; but we do capture exponential growth by focusing on the early data points (representing the exponential phase) for our growth rate calculations. We have now explicitly mentioned this in the methods section “Measuring growth parameters”.

A second concern is the use of the term "tRNA expression levels" in the text in Figure 4. I believe the YAMAT-seq method reports on the fractional contribution of a given tRNA to the total tRNA pool. Thus, since the total tRNA pool is larger in fast-growing cells than in slow-growing cells, a given tRNA may be present at a higher absolute concentration in the fast than in the slow-growing cells but will be reported as "higher in poor" in figure 4, if the given tRNA constitutes a smaller fraction of the total tRNA pool in rich than in poor medium. For this reason, the conclusions regarding the effect of growth medium quality on tRNA levels are not justified.

Thank you for this important point. We agree that our phrasing was incorrect, and we have modified the relevant text and figures accordingly. The fractional contribution of a given tRNA isotype to the total tRNA pool is still useful to compare, and is justified as now rephrased.

Reviewer #2 (Public Review):

Raval et al. by creating a series of deletion mutants of tRNAs, rRNAs, and tRNA modifying enzymes, have shown the importance of gene copy number redundancy in rich media. Moreover, they successfully showed that having too many tRNAs in poor media can be harmful (for a subset of the examined tRNAs). Below, please find my comments regarding some of the methodologies, conclusions, and controls needed to stratify this manuscript's findings.

Figure 2 presents Rrel as a relative measurement (GRmut/GRwt). Therefore, I'm confused as to how Rrel can be negative, as shown in supplemental file 3 (statistics).

We apologize for the confusion. Supplemental file 3 shows details of the statistical analysis (not raw data), and we included the effect size here (mean difference between the WT and the mutant relative growth rate) along with statistical significance. Thus, if the rel R of a given mutant is 1.1, the mean difference would be (1–1.1) = –0.1, meaning that it is performing 10% better than the WT.

The “raw” relative growth rates are provided in source data files (labeled figure-wise), and there are no negative values there, as expected.

We have now explicitly (and separately) referenced the source and statistics data files in the data analysis section in the methods, and in each figure legend. We hope this avoids confusion and makes it easier for readers to find the correct file.

Does Figure 3 show the mean of 4 biological replicates or technical replicates? It should be stated clearly in the legend of figure 3.

All replicates are biological replicates until unless stated otherwise. This is now stated in the methods (lines 185-187), and in the figure legends.

Do all strains (datapoint on figure 3 left panel) significantly perform better than the WT in nutrient downshift? Looking at supplemental file 3 I see this is not the case. Please mark the statistically significant points. I suggest giving each set a different symbol/shape and coloring the significant ones in red.

We had considered indicating statistical significance in the plot, but decided not to do so because it was difficult to show the many potentially useful layers of information without cluttering the plot. One other practical difficulty was that each point in the figure represents two values: one from the upshift (Y axis) and one from the downshift (X axis). For some mutants the fitness difference was significant in only one direction, so it was not straightforward to indicate significance. Further, our main goal here was to show where strains from different deletion Sets (Figure 1) fall in this plot (i.e. which quadrant they occupy), and so we wanted to ensure that points were easily distinguished by Set. In the text we do not include statistically non-significant points in the summary of observed patterns, and refer readers to information on statistical significance provided in the supplemental file.

Another issue is that in the statistics of figure 2 (in supplemental file 3), positive values reflect cases where the mutant performs poorly compared to the WT, while in figure 3 the negative values indicate this. Such discrepancy is not very clear. And again, how can Rrel be negative?

As noted in response to an earlier comment, Rrel values (given in source data files) are not negative, but effect sizes (given in supplemental file with statistics) may be negative or positive since they show differences in the relative growth rate of WT and mutant. We agree that the discrepancy between the calculation of mean difference for Figs 2 and 3 was confusing. We have now fixed this: in both cases, negative mean difference values now indicate that the mutant performs better.

Both axes say glycerol. What about galactose?

The typo has been corrected.

Lines 414-419: The authors state that "all but one had a growth rate that was comparable to WT (16 strains) or higher than WT (10 strains) after transitioning from rich to poor media (i.e. during a nutrient downshift, note data distribution along the x-axis in Fig 3; Supplementary file 3). In contrast, after a nutrient upshift, 11 strains showed significantly slower growth in one or both pairs of media, and only 2 showed significantly faster growth than WT (note data distribution along the y-axis in Fig 3; Supplementary file 3)".

Looking at the Rrel values when transitioning from TB to Glycerol and vice versa suggests no direction in the effect of reducing redundancy. During downshift, four strains perform better, and three strains perform worse than the WT. During upshift, four stains perform better, and six strains perform worse. Only during downshift and upshift from TB to Gal and vice versa give a strong signal.

The authors should write it clearly in the text because the effect is specific to that transition/conditions and not of general meaning is written in the text (e.g., transition from every rich to every poor media and vice versa). I am convinced that the authors see an actual effect when downshifting or upshifting from TB to galactose and vice versa. In that case, the conclusion is that redundancy is good or bad depending on the conditions one used and not as a general theme.

Also, this is true just for some tRNAs, so I don't think the conclusion is general regarding the question of redundancy.

The fitness impacts of altered redundancy are best explained by a combination of multiple factors (in addition to nutrient availability): the number of tRNA genes deleted, number of tRNA gene copies remaining as a backup, availability of wobble or ME as backup, and codon usage. Thus, any of these variables alone would provide only partial explanation for the observed fitness effects of all strains.

In many tRNA deletion strains – especially single gene deletions – redundancy was not significantly lowered by the deletion, as we explain in the results section. These strains were therefore not expected to show major fitness impacts or follow strong nutrient dependent trends, and this is what we observe.

The same is true for nutrient upshift-downshift experiments, where a vast majority of strains were not expected to show a specific pattern because they do not show significant fitness impacts in general, nor do they show a strong correlation in relative fitness impacts vs. growth rate (Figure 1d). In addition, in these experiments the difference between the two media also matters. For example, comparing the maximum WT growth rate, M9 Gal is poorer than M9 Glycerol. Therefore, shifts between TB-Gal are nutritionally more drastic than TB-Gly shifts, and one would expect a larger fitness impact in the former (for strains with significantly altered redundancy). Hence, despite differences across media pairs, our broader conclusions about the impact of redundancy are generalizable as long as redundancy and nutrients are both substantially altered, e.g. due to deletion of 3 tRNA genes, deletion of tRNA+ME, or deletion of multiple rRNA operons.

Figures are indicated differently along the text. Sometimes they are written "figure X", sometimes FigX. Referring to the supplemental figures are also not consistent.

We have now corrected this.

Line 443-444: "In fact, 10 tRNAs were significantly upregulated in the poor medium relative to the rich medium".

This result contradicts the author's hypothesis. If redundancy is bad in poor media because the cells have more tRNAs than they need, the tRNAs level will be downregulated, not upregulated. How do the authors explain this?

This statement referred to the WT strain, and was meant to highlight that (as noted by the reviewer) some tRNAs appear to be upregulated in poor medium, which is counterintuitive. However, as noted by reviewer 1 (see their comment on the interpretation of YAMAT-seq data), we can only infer the relative contribution of each tRNA isotype to the total tRNA pool (rather than absolute up- or down- regulation). Thus, we have removed this specific sentence, and instead we focus on the mismatch between the media-dependent changes in the composition of the tRNA pool and the fitness effects of different tRNA isotypes (lines 475-482).

Line 445-447: "In contrast (and as expected), all tested tRNA deletion strains had lower expression of focal tRNA isotypes in the rich medium (Fig 4B, left panel), showing that the backup gene copies are not upregulated sufficiently to compensate for the loss of deleted tRNAs". It is great that the authors validated the expression in their strains. However, for accuracy, please indicate that it was done in four strains to avoid the impression that they did it in all the strains.

We have now reworded this sentence to remind readers that we measured 4 tRNA deletion strains in this experiment.

Finally, across the manuscript, the authors reveal that deleting some tRNAs or modifying enzymes can be deleterious in rich media or advantageous in poor media. However, I think this result and the conclusions derived from it could be more convincing if the authors would show in a subset of their strains that expressing the deleted tRNAs or modifying enzymes from a plasmid can rescue the phenotype.

Thank you for this suggestion. For a small subset of strains, we now include data showing that complementation from a plasmid indeed rescues the deletion phenotype (Fig 2 – Fig supplement 7).

Reviewer #3 (Public Review):

In this manuscript, Raval et al. investigated the cost and benefit of maintaining seemingly redundant components of the translation machinery in the E. coli genome. They used systematic deletion of different components of the translation machinery including tRNA genes, tRNA modification enzymes, and ribosomal RNA genes to create a collection of mutant strains with reduced redundancy. Then they measured the effect of the reduced redundancy on cellular fitness by measuring the growth rate of each mutant strain in different growth conditions.

This manuscript beautifully shows how maintaining multiple copies of translation machinery genes such as tRNA or ribosomal RNA is beneficial in a nutrient-rich environment, while it is costly in nutrient-poor environments. Similarly, they show how maintaining parallel pathways such as non-target tRNA which directly decodes a codon versus target tRNA plus tRNA modifying enzymes which enable wobble interactions between a tRNA and a codon have a similar effect in terms of cost and benefit.

Further, the authors show the mechanisms that contribute to the increased or reduced fitness following a reduction in gene copy number by measuring tRNA abundance and translation capacity. This enables them to show how on one hand reduced copy numbers of tRNA genes result in lower tRNA abundance in rich growth media, however in nutrient-limiting media higher copy number leads to increased expression cost which does not lead to an increased translation rate.

Overall, this work beautifully demonstrates the cost and benefits of the seemingly redundant translation machinery components in E. coli.

Thank you for the clear summary and encouraging comments.

However, in my opinion, this work’s conclusion should be that the seeming redundancy of the translation machinery is not redundant after all. As mentioned by the authors, it is known that tRNA gene copy number is associated with tRNA abundance (Dong et al. 1996, doi: 10.1006/jmbi.1996.0428), this effect is also nicely demonstrated by the authors in the section titled “Gene regulation cannot compensate for loss of tRNA gene copies”. Moreover, this work demonstrates how the loss of the seeming redundancy is deleterious in a nutrient-rich environment. Therefore, I believe the experiments presented in this work together with previous works should lead to the conclusion that the multiple gene copies and parallel tRNA decoding pathways are not redundant but rather essential for fast growth in rich environments.

The point is well taken. However, as described in the introduction, here we focus on functional redundancy at the cellular level, where there are multiple ways of achieving the same translation rate. Hence we say that translation components are redundant at this level of analysis. One of the key conclusions from our work is that such redundancy is context-dependent, i.e. it is essential when rapid growth is possible, but is costly and dispensable otherwise. Therefore, we show that the definition of redundancy itself changes with environmental conditions.

The following analogy may help convey this. There may be many ways to reach a flight on an airport: multiple entrances, multiple check-in and security check counters, multiple boarding gates, etc. On a deserted airport these may seem redundant and even costly to maintain. On the other hand, they have a utility when traffic is high. Hence even though from a purely architectural perspective the multiple routes are redundant, from a utilitarian perspective it depends on the flux of passengers.

Author Response

Reviewer 2 (Public Review):

The paper addresses the question of how brain circuits associate stimuli onto abstract representations, and how both the neuronal activity and the synaptic connectivity change during this process. To do so, the authors make use of a feedforward network model that learns to map stimuli vectors onto two categories by means of gradient descent. They show that the model successfully learns the abstract classes in a simple and context-dependent categorisation task. The authors analyse a number of measures, like category and context selectivity to link their results to experimental findings. Moreover, they analyse the network thoroughly and unravel network and task properties that may underlie previous, seemingly contradictory experimental findings. The paper is very well written, the analyses and mathematical derivations are very thorough and the results are convincing. However, the work and its presentation would benefit from a few changes:

1) The paper may benefit from a more thorough discussion on how the results fit into the current literature (neuroscience and machine learning) and how the findings may generalise to more complex tasks and network structures (Dale’s principle, including recurrent/feedback connections, more than two categories, more than one hidden layer, alternatives to gradient descent).

2) While the simulations and detailed analyses in the results and methods section are very convincing, some claims should be also supported by more intuitive explanations so that a broader audience can be reached.

3) The introduction to the context-dependent task may need to be revised because as now the difference to the simple task presented first is not immediately clear.

4) It would be nice if their findings could be related back to the experimental literature more qualitatively. While the authors mention the contradictory findings in monkey and rat PFC vs. monkey LIP in their introduction, a thorough comparison with those findings is missing.

We thank the reviewer for his detailed assessment and his supportive words. We hope that our revision addresses your suggestions. Concerning point 4: we agree with the reviewer that a thorough comparison with experimental findings would be important, and is currently missing. A thorough comparison would require, however, a number of additional steps that we feel lie beyond the scope of this manuscript (adapt the tasks to each different experimental setup, e.g. by increasing the number of categories and changing the structure of context-dependent associations; re-analyse experimental data).

We have thus decided to leave this major effort for future work.

Author Response

Public Evaluation Summary

The authors aim to tackle a fundamental question with their study: whether there is a direct age-associated increase of transcriptional noise. To investigate this question, they develop tools to analyze single-cell sequencing data from mouse and human aging datasets. Ultimately, application of their novel tool (Scallop) suggests that transcriptional noise does not change with age, changes in transcriptional noise can be attributed to other sources such as subtle shifts in cell identity. This study is in principle of broad interest, but it currently lacks a definitive demonstration of the robustness of Scallop. Systematic testing of this new package would ultimately strengthen the key conclusion of the work and give additional users more confidence when using the tool to estimate expression noise.

We have now attempted to further demonstrate the robustness of Scallop by performing a more systematic analysis and a side-by-side comparison to other existing methods using a set of artificially generated datasets. These analyses have resulted in the inclusion of six supplementary figures that are presented in the subsections Scallop membership score accurately identifies transcriptionally noisy cells, Ability to detect noisy cells within cell types, Effect of cellular composition, Effect of dataset size, Effect of feature expression and Effect of cell type marker expression within the Results section of the revised manuscript.

We have also included a supplementary figure showing an in-depth analysis of a dataset where ageassociated increase in transcriptional noise was detected using alternative methods, but whose closer dissection has revealed that the difference in noise is due to a single donor and to the choice of methods. We discuss this is in the subsection Distance-to-centroid methods detect transcriptionally stable cell subtypes as transcriptional noise within the Results section.

Finally, we have revised the manuscript to clarify the main points raised by the reviewers: the definition of transcriptional noise, the reasoning behind the choice of the single-cell aging datasets and Leiden’s rationale. Also, we have expanded the description of the method to make the definition of membership score more clear to the readers, and discussed the implications of our main findings (a lack of evidence for age-related transcriptional noise) in the broader context of theories of aging.

Reviewer #1 (Public Review):

In the present study, Ibanez-Sole et al evaluate transcriptional noise across aging and tissues in several publicly available mouse and human datasets. Initially, the authors compare 4 generalized approaches to quantify transcriptional noise across cell types and later implement a new approach which uses iterative clustering to assess cellular noise. Based on implementation of this approach (scallop), the authors survey noise across seven sc-seq datasets relevant for aging. Here, the authors conclude that enhanced transcriptional noise is not a hallmark of aging, rather changes in cell identity and abundances, namely immune and endothelial cells. The development of new tools to quantify transcriptional noise from sc-seq data presents appeal, as these datasets are increasing exponentially. Further, the conclusion that increased transcriptional noise is not a defined aspect of aging is clearly an important contribution; however, given the provocative nature of this claim, more comprehensive and systematic analyses should be performed. In particular, the robustness and appeal of scallop is still not sufficiently demonstrated and given the complexity (multiple tissues, species and diverse relative age ranges) of datasets analyzed, a more thorough comparison should be performed. I list a few thoughts below:

Initially, the authors develop Decibel, which centralizes noise quantification methods. The authors provide schematics shown in Fig 1, and compare noise estimates with aging in Fig 2 - Supplement 2. Since the authors emphasize the necessary use of scallop as a ”better” pipeline, more systematic comparisons to the other methods should be made side-by-side.

We thank the reviewer for their positive assessment of the manuscript and their suggestions. We agree that side-by-side benchmarking of Scallop with the methods implemented in Decibel, as well as a more thorough analysis on the effect of different features such as dataset size, cellular composition, etc. might have on the output of Scallop will reinforce the main points of the manuscript. To experimentally respond to these requests, we took advantage of a set of four artificial datasets previously generated by us with the R package splatter (v1.10.1; as described in Ascensión et al. [1]). In the present work, we first run a side-by-side comparison between Scallop and two distance-to-centroid (DTC) methods on the four artificial datasets with increasing degrees of transcriptional noise present in them (the novel data are included as Figure 1 – Figure supplement 1 in the revised manuscript). Then, we compared Scallop to one DTC method regarding their ability to detect noisy cells in different cell types (Figure 1 – Figure supplement 2). Finally, we implemented four simulations to test the effect of the following features on the performance of Scallop: cellular composition (Figure 1 – Figure supplement 3), dataset size (Figure 1 – Figure supplement 4), number of genes (Figure 1 – Figure supplement 5) and marker gene expression (Figure 1 – Figure supplement 6). A summary of these results follows.

Side-by-side comparison of Scallop vs DTC methods

Each of the four artificial datasets used consists of 10K cells, from 9 populations, named Group1 to Group9, with the following relative abundances: 25, 20, 15, 10, 10, 7, 5.5, 4, and 3.5%, respectively. The four datasets only differ in the de.prob parameter used in their generation. The de.prob parameter determines the probability that a gene is differentially expressed between subpopulations within the dataset. The greater the de.prob value, the more differentially expressed genes there will be between clusters, meaning that the different cell types present in the dataset will cluster in a more robust way. Decreasing the value of de.prob results in datasets with noisy cells, with populations that do not have such a strong transcriptional signature. In order to study how Scallop can capture the degree of robustness with which cells of the same cell type cluster together, we selected four de.prob values (0.05, 0.016, 0.01 and 0.005) and measured transcriptional noise using Scallop and two DTC methods, the whole transcriptome-based Euclidean distance to cell type mean and the invariant gene-based Euclidean distance to tissue mean expression. These two methods were selected because GCL does not yield a transcriptional noise measure per cell, so no comparisons can be made with respect to the amount of noisy cells the method is able to detect within a cluster. Similarly, comparing Scallop to the ERCC spike in-based method was not possible for artificial datasets. Importantly, these analyses showed that Scallop, unlike DTC methods, was able to discern between the core transcriptionally stable cells within each cell type cluster from the more noisy cells that lie in between clusters (provided in the Figure 1 - Supplement 1 of revised manuscript).

Effect of dataset features on the performance of Scallop

We simulated five artificial datasets with the same nine cell type populations but whose relative abundances were different between datasets. We used the imbalance degree (ID) to measure class imbalance in each of them and to make sure that the selected cell compositions represented a wide range of imbalance degrees (to this end, we explored ID values between 1.2 and 5.3). The ID provides a normalized summary of the extent of class imbalance in a dataset in so-called ”multiclass” settings, that is to say, where more than two classes are present. It was specifically developed to improve the commonly used imbalance ratio (IR) measurement, whose calculation only considers the abundance of the most and the least popular classes and which gives the same summary for datasets with different numbers of minority classes. The presence of multiple minority classes is not uncommon in single-cell RNAseq datasets, as tissues might contain several rare cell types. We observed that the transcriptional noise measurements provided by Scallop were very robust to changes in imbalance degree (see Figure 1 - Supplement 3), both in qualitative and in quantitative terms. For instance, Group2 and Group8 were always detected as the most stable and noisiest cell types, respectively, regardless of their relative abundance in the dataset, and their average percentage of noise had little variation between different ID values: it ranged between 0-0.14% (Group2) and 16-18% (Group8).

The effect of dataset size (number of cells) and the number of genes was evaluated by generating versions of an artificial dataset where cells/genes had been subsampled from an original artificial dataset (the one generated with de.prob=0.001). We tested datasets sized 1,000-10,000 cells and with a number of genes between 5,000 and 14,000. Dataset size had nearly no impact on the transcriptional noise measurements provided by Scallop (Figure 1 - Supplement 4 of the revised manuscript). The average percentage of transcriptional noise per cell type remained within a narrow range as we implemented a ten-fold increase in dataset size. Perhaps more strikingly, removing the expression of most genes did not substantially impact transcriptional noise measurements per cell type (Figure 1 - Supplement 5). The variation when removing half of the genes (7,000 genes) was minimal, and we did not see important changes in transcriptional noise measurements unless over 60% of the genes from the original dataset were removed. For example, Figure 1 - Supplement 5C shows that noise measurements suffer important variations when removing 8,000 and 9,000 genes (and therefore keeping 6,000 and 5,000 genes, respectively), but only some cell types (Groups 4, 7, 8 and 9) were affected by these variations.

In order to measure the effect marker gene expression has on the membership with which cells are assigned to their cell type cluster, we ran a simulation where the top 10 markers for a cell type were removed from the dataset one by one, so that the first simulation lacked the expression of the Top1 marker, the second simulation had the effect of the first 2 markers removed (Top1 and Top2), and so on. Then, we ran Scallop on each of the resulting datasets and observed a steady increase in transcriptional noise associated with that cell type. This provided evidence that the strength of cell type marker expression in a cluster is directly related to its transcriptional stability (or lack of transcriptional noise). We included the result of this experiment in the revised version of the manuscript (Figure 1 - Supplement 6).

In conclusion, by using artificially generated datasets where the ground truth (cell type labels, degree of noise, etc) was known, the newly provided systematic analyses showed that Scallop had a remarkably robust response to said changes in dataset features, further reinforcing the manuscript conclusions.

For example, scallop noise estimates (Fig 2) compared to other euclidean distance-based measures (Fig 2 supplement 2) looks fairly similar.

It is true that some datasets show similar trends regardless of the transcriptional noise quantification method. For instance, the murine brain dataset by Ximerakis et al. shows no overall change in noise between the age groups across different methods. However, we do observe important differences in other examples. This is the case of the human pancreas dataset by Enge et al. and the human skin dataset by Solé-Boldo et al., where not only the magnitude but also the directionality of the trend are different depending on the method used to measure noise. In the former, three methods (Scallop, invariant gene-based Euclidean distance to average tissue expression and GCL) show an age-related increase in noise, whereas one method (whole transcriptome-based Euclidean distance to the cell type mean) shows a decrease in noise. In the latter, two methods (Scallop and GCL) yield a decrease in noise and the two DTC methods measure a mild increase in noise. These inconsistencies can now be reconciled with our proposed explanation that said ”noise” may actually be referring to substantially different biology in the diverse experimental settings.

Are downstream observations (ex lung immune composition changes more than noise) supported from these methods as well? If so, this would strengthen the overall conclusion on noise with age, but if not, it would be relevant to understand why.

Studying changes in cell type composition in the lung and other aged tissues would be highly pertinent. Nevertheless, we have measured changes in cell type composition using only one method that is based on Generalized Linear Models, covered in the subsection Age-related cell type enrichment of the Methods. The methods that we have compared in our study (DTC methods, ERCC-based methods, GCL, etc.) were all designed to measure transcriptional noise, but not changes in cell type composition.

Whether the effects of cell type composition changes are bigger than changes in noise for the rest of the methods used to measure noise was probably not clear enough in the original manuscript. We found no evidence for an increase in noise associated with aging, regardless of the method used. Although not included in the manuscript, we did generate heatmaps similar to the one shown in Figure 3B for each of the noise quantification methods. However, as the heatmap on the right side (the one showing cell type enrichment) was identical in each figure, we considered them to be redundant and decided not to include them, since they did not provide any additional insight besides giving more examples of lack of evidence for transcriptional noise, this time at the cell type level. We consider that the lack of evidence was already well demonstrated in the previous analyses (Figure 2 and Figure 2 - Supplement 2.

Similarly, the ’validation of scallop seems mostly based on the ability to localize noisy vs stable cells in Fig 1 supplement 1 and relative robustness within dataset to input parameters (Fig 1 supplement 2). A more systematic analysis should be performed to robustly establish this method. For example, noise cell clustering comparisons across the 7 datasets used. In addition, the Levy et all 2020 implemented a pathway-based approach to validate. Specifically, surrogate genes were derived from GCL value where KEGG preservation was used as an output. Similar additional types of analyses should be performed in scallop.

We believe that this legitimate concern is now solved with the newly included data. In particular, with the systematic comparison between Scallop and DTC methods on three artificially generated datasets with different degrees of transcriptional noise provided in Figure 1 - Supplement 2. The ability of Scallop to detect cells that are particularly noisy within a cell type, or cells that lie between cell types, may represent its biggest advantage with respect to other methods. DTC methods fail to discern between stable and noisy cells within cell types. Also, in our analysis, DTC methods were unable to distinguish between cell types that have a marked transcriptional program (which systematically cluster together) and those that have a less clear transcriptomic identity (which have at least part of their cells be assigned to other cell types across bootstrap iterations). However, comparing the performance of Scallop on the same datasets showed that our method was able distinguish between the two cases.

The conclusion that immune and endothelial cell transcriptional shifts associate more with age than noise are quite compelling, but seem entirely restricted to the mouse and human lung datasets. It would be interesting to know if pan-tissues these same cell types enrich age-related effects or whether this phenomenon is localized.

We agree with the reviewer that it would be very interesting to see whether a change in cell type composition (and particularly, an increase in abundance of immune cell types) is observed in aged tissues other than the lung. Qualitative cell type composition changes in the aging lung have been described in the literature [5]. Specifically, the higher abundance of immune cell types was observed in a single-nucleus RNAseq dataset of cardiopulmonary cells in Macaca fascicularis [6]. However, we believe that trying to answer the question whether this phenomenon holds in other tissues would require a systematic analysis of several datasets for each tissue with a sufficient number of donors/individuals in each of them. This is because our approach to measure age-associated cell type enrichment using generalized linear models relies heavily on having multiple biological replicates for each age group. Unfortunately, this is not the case for most published single-cell RNAseq datasets of aging. In any case, we have toned down the last sentence in the subsection Changes in the abundance of the immune and endothelial cell repertoires characterize the human aging lung by making it more clear that our claim regarding changes in the cellular composition of aged tissues is based on lung datasets (the text in italics represents what was added in the revised version of the manuscript):

"Even though the evidence for changes in tissue composition are based on a single tissue, we hypothesize that these facts may have influenced previous analyses of transcriptional noise associated with aging."

As discussed in the original manuscript, there is evidence published by other groups pointing out to pantissue changes in cellular composition with age, which undoubtedly will influence those analyses that did not pay attention to cellular composition changes in the datasets that they compared. Cellular composition is in fact a very important aspect that has been greatly overlooked. In fact, only one [7] out of the seven articles that had measured transcriptional noise in aging (the datasets used in Figure 2) had attempted to remove its effect by subsampling cells to balance compositions between age groups prior to their noise analysis. In any case, we do not believe this is the only phenomenon underlying the purported increase in transcriptional noise associated with age. Each dataset will most probably have different issues that the authors originally misread as an increase in noise or loss of cellular identity of a particular organ or tissue. As an additional example of such phenomena, we have now included a re-analysis of the data by Enge et al. [3] on ”noisy” β-cells in the aged human pancreas (Figure 5–Figure supplement 2 of the revised manuscript). In this case, rather than observing an age-dependent pattern, the 21-year-old donor presents much lower transcriptional noise values than the rest of the donors. However, there is no significant difference between the 22-year-old donor and the rest of the donors. We conclude that the statistically significant differences between the ”young” and ”old” age categories can be attributed to the abnormal noise values obtained for the 21-year-old donor, of uncertain origin. Finding out all causes of apparent transcriptional noise in other organs and tissues would be too lengthy, and certainly out of scope for the present manuscript.

Related to these, there does not seem to be a specific rationale for why these datasets (the seven used in total or the lung for deep-dive), were selected. Clearly, many mouse and human sc-RNA-seq datasets exist with large variations in age so expanding the datasets analyzed and/or providing sufficient rationale as to why these ones are appearing for noise analyses would be helpful. For example, querying ”aging” across sc-seq datasets in Single cell portal yields 79 available datasets: https://singlecell.broadinstitute. org/single_cell?type=study&page=1&terms=aging&facets=organism_age%3A0%7C103%7Cyears.

We now realize that the reasoning behind our selection of aging datasets was not sufficiently clear in the original manuscript. We thank the reviewer for pointing out this omission. We have made a more explicit reference to Appendices 2, 3, 4 and 6 in the revised manuscript. The seven selected scRNAseq datasets are those where transcriptional noise had originally been measured by the authors, using the computational methods that we later implemented in Decibel. Our aim was to first recapitulate previous reports of transcriptional noise using our novel method (Scallop). Thus, we downloaded all publicly available scRNAseq datasets of aged tissues where transcriptional noise had explicitly been measured. Some of them had reported an increase in transcriptional noise only in some cell types (for instance, the human aged pancreas dataset by Enge et al. [3]), whereas others found an increase in most cell types [7]. Appendix 2 summarizes the main features of those seven datasets (tissue, organism and number of cells) and provides information on whether an increase in transcriptional noise was observed in the original article where they were published. Additionally, the ”scope” column indicates where that increase was found (in which cell types), and the ”Method” column briefly describes the computational method used to measure transcriptional noise in that article. Appendix 3 provides information on the final datasets that were used in our analysis (Figure 2). Not every sample from the original dataset was included, so the inclusion criteria are specified there, as well as the number of cells, individuals and age of each of the cohorts. Appendix 4 shows the abnormal count distribution of two samples that were discarded from the Kimmel lung dataset. As for the selection of lung for the deep dive, the reason was that this was the organ with most datasets available, both for mouse and human. Appendix 6 provides information on the number of cells and donors per age cohort in the human lung datasets included in this study.

We have included the following sentence in the Increased transcriptional noise is not a universal hallmark of aging subsection in the Results:

"We provide a summary of the main characteristics of each dataset, as well as the findings regarding transcriptional noise obtained in each of the original studies, whether changes in transcriptional noise were restricted to particular cell types, and the computational method used to measure noise (see Appendix 2)."

The analysis that noise is indistinguishable from cell fate shifts is compelling, but again relies on one specific example where alternative surfactant genes are used as markers. The same question arises if this observation holds up to other cell types within other organs. For example the human cell atlas contains over dozens of tissue with large variations in age (https://www.science.org/doi/10.1126/science. abl4290).

We sympathize with this comment but hope that the reviewer will agree with us that providing an additional example of different phenomena originally reported as ”transcriptional noise” (in this case in aged human pancreas; see Figure 5 – Figure supplement 2), but actually reflecting something else, may be sufficient to prevent interested readers. In our opinion, it is likely that diverse phenomena will underlie the purported increases in transcriptional noise, and a re-analysis should be made case-by-case. We can only hope that researchers in the field re-analyze the available aging datasets in this new light.

Reviewer #2 (Public Review):

In this manuscript, Ibanez-Sole et al. focus on an important open question in ageing research; ”how does transcriptional noise increase at the cellular level?”. They developed two python toolkits, one for comparison of previously described methods to measure transcriptional noise, Decibel, and another one implementing a new method of variability measure based on cluster memberships, Scallop. Using published datasets and comparing multiple methods, they suggest that increased transcriptional noise is not a fundamental property of ageing, but instead, previous reports might have been driven by age-related changes in cell type compositions.

I would like to congratulate the authors on openly providing all code and data associated with the manuscript. The authors did not restrict their paper to one dataset or one approach but instead provided a comprehensive analysis of diverse biology across murine and human tissues.

While the results support their main conclusions, the lack of robustness/sensitivity measures for the methods used makes it difficult to judge the biology.The authors use real data to compare between methods but using synthetic data with known artificial ’variability’ across cell clusters can first establish the methods, which would make the results more convincing and easier to interpret. Despite the comprehensive analysis of biological data, a detailed prior description of how the methods behave against e.g. the number of cells in each cell type cluster, the number of cell types in the dataset, and % feature expression, would make the paper more convincing. Once the details of the method is provided, the python toolkit can be widely used, not limited to the ageing research community. I am also concerned that a definition of ’transcriptional noise’ (e.g. genome-wide noise, transcriptional dysregulation in cell-type-specific genes, noise in certain pathways) and its interpretation with regard to the biology of ageing is missing. Differences in different methods could be explained by the different biology they capture. Moreover, the interpretation of a lack of different types of variability may not be the same for the biology of ageing.

Increased transcriptional noise is compatible with genomic instability, loss of proteostasis and epigenetic regulation. Showing a lack of consistent transcriptional noise can challenge the widespread assumptions about how these hallmarks affect the organism. Overall, I found the paper very interesting and central to the field of ageing biology. However, I believe it requires a more detailed description of the methods and interpretations in the context of biology and theories of ageing.

We thank the reviewer for their positive assessment of the manuscript and their suggestions. We respond to each of the specific comments below.

Major comments

1) The concept of transcriptional noise is central to the manuscript; however, what the authors consider as transcriptional noise and why is not clear. Genome-wide vs. function or cell-type specific noise could have different implications for the biology of ageing. In line with this, a discussion of the findings in the context of theories of ageing is necessary to understand its implications.

We thank the reviewer for pointing out the lack of clarity in this key point. The use of the ”transcriptional noise” term in the literature is quite heterogeneous, and we agree that the lack of a consensus definition may be confusing to the reader. For this reason, we adopted in the introduction the definition by Raser and O’Shea [8] as ”the measured level of variation in gene expression among cells supposed to be identical”, i.e. the sum of both intrinsic and extrinsic noise as previously defined by Swain and colleagues [9, 10]. In our opinion, this is generally what the literature of age-associated transcriptional noise is referring to.

With Scallop, we aimed to translate this concept to the context of single-cell RNAseq datasets, where clusters obtained using a community detection algorithm are typically annotated as distinct cell types.

Therefore, we aimed to measure transcriptional noise here defined as ”lack of membership to cell type clusters”. When running a clustering algorithm iteratively, if a cell is not unambiguously assigned to the same cluster, we consider it to be noisy. Conversely, when a cell consistently clusters with the same group of cells, we consider it to be stable. The membership score we use as a measure of stability is the frequency with which any given cell was assigned to the same cluster across all iterations.

We have included in the Results section an explicit reference to the Methods subsection that explains how Scallop works in detail, so that the readers can easily find that information:

"A detailed description of the three steps of the method (bootstrapping, cluster relabeling and computation of the membership score) is provided in the Scallop subsection in the Methods."

Additionally, we have now realized that the formula to compute the membership score might be more easily understood if we renamed the freq_score as freq_score(c), to make it clear that each cell is assigned a score. Also, we have used n and m instead of i and j in this notation, to avoid confusing the readers with the notation used in the previous section, where i and j represented the i-th and j-th bootstrap iterations. Finally, we have included a small paragraph to clarify what each component of the formula refers to. Below we show the formula and text included in the Methods section of the revised manuscript:

"Where |cn| is the number of times cell c was assigned to the n-th cluster, and Pm∈clusters |cm| is the sum of all assignments made on cell c, which is the same as the number of times cell c was clustered across bootstrap iterations."

Thus, and in order to accommodate this reviewer’s concerns, we have now included this exact definition of how we measure noise plus a statement making clear that we refer to the sum of both intrinsic and extrinsic noise aspects, with no distinction among them.

Similarly, we had discussed our findings in the framework of different theories of aging, such as their potential relationship to some of the established hallmarks of aging (genomic instability, epigenetic deregulation and loss of proteostasis), as well as with more recent theories of aging such as cell type imbalance in aged organs [11] and inter-tissue convergence [12]. However, it is now clear to us that this was not enough so we have now expanded these paragraphs to make our understanding of the work implications better understood. More specifically:

"Our results suggest that transcriptional noise is not a bona fide hallmark of aging. Instead, we posit that previous analyses of noise in aging scRNAseq datasets have been confounded by a number of factors, including both computational methods used for analysis as well as other biology-driven sources of variability."

2) While I found the suggested method, Scallop, quite exciting and valuable, I would suggest including a number of performance/robustness measures (primarily based on simulations) on how sensitive the method is to the number of cells in each cell type (cellular composition), misannotations, % feature expression (number of 0s) etc.:

We have analyzed the effect of cellular composition and the percentage of feature expression by using artificially generated datasets (see Figure 1 - Supplements 3 and 5, respectively; and section Effect of dataset features on the performance of Scallop in the response to reviewer #1). Although studying the effect of misannotations on downstream analysis is important, we believe that Scallop was already designed so that its effects could be avoided, since the membership is measured for each cluster (and not for each cell type label). That is to say, a reference clustering is obtained at the beginning of the pipeline and memberships are computed using that output as a reference, which means Scallop noise values attributed to each cell are not affected by the original labeling of the dataset.

The output of these analyses reinforced our original conclusions, and it is now included in the Results section:

"In order to characterize and validate our method for transcriptional noise quantification, we conducted three types of analyses. First, we used artificially generated datasets containing various degrees of transcriptional noise to compare the performance of Scallop and DTC methods side-by-side, regarding their ability to measure transcriptional noise and detect noisy cells within cell types. Next, we ran simulations using artificial datasets in order to study the effect of a number of dataset features on the performance of Scallop: cellular composition, dataset size, number of genes and marker expression. Finally, we graphically evaluated the output of Scallop on a dataset of human T cells, we analyzed its robustness to its input parameters, and we studied the relationship between membership and robust marker expression, using a PBMC dataset."

2.1) Most importantly, knowing that cell-type composition changes with age, it is important to know how sensitive community detection is to the number of cells in each cell type. While the average can be robust, I wonder if the size of the cell-type cluster affects membership (voting).

We have included an analysis on a set of artificial datasets with different cellular compositions to evaluate the performance of Scallop in the presence of different degrees of class imbalance (see Figure 1 - Supplement 3). We explain the output of this analysis, which reinforces the algorithm’s robustness, in the Results section:

"Next, we ran a series of simulations on artificially generated datasets to evaluate the performance of Scallop in the presence of different levels of class imbalance, dataset size, number of genes, and different degrees of expression of cell type markers. Our analysis showed that Scallop was remarkably robust to changes in cellular composition (see Figure 1 - Supplement 3). Both the average percentage of noise and the distribution remained unchanged for a wide range of class imbalance degrees. Similarly, altering the dataset size (number of cells) and the number of genes of an artificial dataset did not cause any major changes on the transcriptional noise values attributed to each cell type (see Figure 1 - Supplements 4 and 5). Additionally, we conducted an analysis where we identified the 10 most differentially expressed gene markers for a cell type and measured the transcriptional noise associated with that cell type as we removed the expression of those genes from the dataset (Figure 1 - Supplement 5). Transcriptional noise steadily increased as we removed the effect of the top marker genes that defined the cell type under study (see Figure 1 - Supplement 5B). This experiment provides further evidence on how strong marker expression is related to robust cell type identity and how the lack of it results in transcriptional noise."

3) Although the Leiden algorithm is widely used by many single-cell clustering methods, since the proposed methodology is heavily dependent on clustering, I suggest including a description of the Leiden algorithm.

We agree that understanding how community detection algorithms in general –and Leiden in particular– work is crucial to understand the core of the paper, so we have included a brief introduction to these methods in the Methods section, at the beginning of the Scallop subsection:

Leiden is a graph-based community detection algorithm that was designed to improve the popular Louvain method [13]. Graph-community detection methods take a graph representation of a dataset. In the context of single-cell RNAseq data, shared nearest neighbor (SNN) graphs are commonly used. These are graphs whose nodes represent individual cells and edges connect pairs of cells that are part of the K-nearest neighbors of each other by some distance metric. The aim of community detection algorithms like Leiden is to find groups of nodes that are densely connected between them, by optimizing modularity. For a graph with C communities, the modularity (Q) is computed by taking, for each community (group of cells), the difference between the actual number of edges in that community (ei) and the number of expected edges in that community ( K2/1/2m).

Where r is a resolution parameter (r > 0) that controls for the amount of communities: a greater resolution parameter gives more communities whereas a low resolution parameter fewer clusters. Since maximizing the modularity of a graph is an NP-hard problem, different heuristics are used, and Leiden has shown to outperform Louvain in this task both in terms of quality and speed [14]. However, users can choose to run the Louvain method instead by setting the parameter clustering="louvain" in the initialization of the Bootstrap object.

3.1) Most importantly, the authors comment that they found stronger expression of cell-type specific markers in the cells with high membership values - is it already a product of the Leiden algorithm that it weighs highly variable (thus cell-type specific) features higher - resulting in better prediction of cell-types for cells with strong cell-marker expression? It is important to make a description of transcriptional noise at this stage as it could be genome-wide or more specific to cell-type markers. Can authors provide any support that their method can capture both?

We agree with the reviewer that finding a stronger expression of cell-type markers in cells with high membership values is indeed something we expected. The graph representation of the dataset taken as input by Leiden is built after running highly variable gene detection and PCA. The neighbors of each cell are detected based on the expression of genes that are highly variable, as the reviewer pointed out, so genes that are differentially expressed between cells are more likely to contribute to the clusters found by Leiden.

Whether Scallop measures genome-wide or cell type-specific noise (or a mixture of both) is a very interesting question. Clusters in single-cell RNA sequencing datasets are often mainly driven by the presence/absence of a few cell type markers, rather than changes in expression levels of broader sets of genes. Moreover, it has been shown that single-cell RNAseq datasets generally preserve the same population structure even after data binarization [15]. This is a consequence of the sparsity of single-cell RNAseq datasets. In our case, any difference in expression between one cluster vs the rest of the cells in the dataset –be it the expression of a gene that was not detected in the rest of the cells or a higher expression of a gene whose presence is weaker in other clusters– will certainly have an impact on the output of every downstream analysis, from clustering to dimensionality reduction. The influence of the expression of cell type-specific markers on Scallop membership has been demonstrated in several analyses. First, the simulation where we measured the impact of removing the 10 most defining markers for a particular cell type on transcriptional noise measurements (included in the Figure 1 - Supplement 6 of the revised manuscript). Also, Figure 5 provides evidence that the differential expression of a handful of genes (in this case, genes coding for surfactant proteins) can have an impact on the clustering solutions obtained for a set of human alveolar macrophages, and this in turn influences the membership scores obtained with Scallop. In essence, Scallop merely provides a measure of the robustness of clustering at the single-cell level, so any type of transcriptional noise might have an impact on Scallop memberships, provided it is sufficiently strong to influence the output of the clustering algorithm used. In other words, the fact Scallop membership captures a mixture of both types of noise (genome-wide and that associated with cell type-specific markers) is a consequence of the influence both types of noise have on clustering.

4) The authors conclude that Scallop outperforms other methods through the analysis of biological data, where there is no positive and negative control. I suggest creating synthetic datasets (which could be based on real data), introducing different levels of noise artificially (considering biological constraints like max/min expression levels) and then testing the performance where the truth about each dataset is known. Otherwise, the definitions of noisy and stable cells, regardless of the method, are arbitrary.

Our initial focus was on biological datasets, were no positive and negative controls regarding transcriptional noise could be used, but we agree in the need of including an analysis using simulations on artificial datasets. We analyzed artificially generated datasets with known degrees of transcriptional noise in order to evaluate the performance of Scallop on a setting where the ground truth is known beforehand. The way we modeled transcriptional noise was by tuning the de.prob parameter, which determines the probability that a gene will be differentially expressed between clusters. The creation of these datasets is explained in detail in the Methods section of the revised manuscript, and specifically in the subsections Performance of Scallop and two DTC methods on four artificial datasets with increasing transcriptional noise. and Ability to detect noisy cells within cell types.

We have now included the following section in the Results:

"We compared the output of Scallop and two DTC methods (the whole transcriptome-based Euclidean distance to average cell type expression and the invariant gene-based Euclidean distance to average tissue expression) on four artificially generated datasets containing various levels of transcriptional noise. The analysis showed that Scallop, unlike DTC methods, was able to discern between the core transcriptionally stable cells within each cell type cluster from the more noisy cells that lie in between clusters (see Figure 1 - Supplement 1). We then compared one of the DTC methods to Scallop regarding their ability to detect noisy cells within each of the cell types, by plotting the top 10% noisiest and top 10% most stable cells and (see Figure 1 - Supplement 2A). Analyzing the distribution of noise values for each cell type separately revealed that Scallop can distinguish between clusters that mainly consist of transcriptionally stable cells from noisier clusters that do not have such a distinct transcriptional signature (Figure 1 - Supplement 2B."

Reviewer #3 (Public Review):

In this manuscript, Ibáñez-Solé et al aim to clarify the answer to a very basic and important question that has gained a lot of attention in the past ∼5 years due to fast-increasing pace of research in the aging field and development/optimization of single-cell gene expression quantification techniques: how does noise in gene expression change during the course of cellular/tissue aging? As the authors clearly describe, there have been multiple datasets available in the literature but one could not say the same for the number of available analysis pipelines, especially a pipeline that quantifies membership of single cells to their assigned cell type cluster. To address these needs, Ibáñez-Solé et al developed: 1. a toolkit (named Decibel) to implement the common methods for the quantification of age-related noise in scRNAseq data; and 2. a method (named Scallop) for obtaining membership information for single-cells regarding their assigned celltype cluster. Their analyses showed that previously-published aging datasets had large variability between tissues and datasets, and importantly the author’s results show that noise-increase in aging could not be claimed as a universal phenotype (as previously suggested by various studies).

We thank the reviewer for their positive assessment of the manuscript and their suggestions.

Comments:

1) In two relevant papers (doi.org/10.1038/s41467-017-00752-9anddoi.org/10.1016/j.isci. 2018.08.011), previous work had already shown what haploid/diploid genetic backgrounds could show in terms of intercellular/intracellular noise. Due to the direct nature of age/noise quantification in these papers, one cannot blame any computational pipeline-related issues for the ”unconventional” results. The authors should cite and sufficiently discuss the noise-related results of these papers in their Discussion section. These two papers collectively show how the specific gene, its protein half-life and ploidy can lead to similar/different noise outcomes.

We agree that we have failed to mention and sufficiently discuss the effects of measuring transcriptional noise from data generated via destructive experimentation, where no longitudinal analyses are possible. As aforementioned in the response to other reviewers, the body of literature on transcriptional noise is quite wide and based on heterogeneous assumptions. We have focused our efforts in measuring actual noise in scRNAseq aging datasets, which by definition imply sampling of different cells and thus make assumptions at the population level. We believe our results provide a different and interesting perspective into transcriptional noise and aging, but we agree with this reviewer in the need to discuss our findings in the context of other attempts to measure transcriptional noise in a more direct way. We have now included a brief discussion of the work by Sarnoski et al. and Liu et al.. This point is explained in more detail later in the letter.

2) While the authors correctly put a lot of emphasis on studying the same cell type or tissue for a faithful interpretation of noise-related results, they ignore another important factor: tracking the same cell over time instead of calculating noise from single-cell populations at supposedly-different age points. Obviously, scRNAseq cannot analyze the same cell twice, but inability to assess noise-in-aging in the same cell over time is still an important concern. Noise could/does affect the generation durations and therefore neighboring cells in the same cluster may not have experienced the same amount of mitotic aging, for example. Also, perhaps a cell has already entered senescence at early age in the same tissue. This caveat should be properly discussed.

The distinction between intrinsic and extrinsic noise and the impossibility to discern between the two in destructive experiments is a relevant point that we have now included in the Discussion (the newly added text is shown in italics):

"Transcriptional noise could be related to genomic instability [18], epigenetic deregulation [19, 20] or loss of proteostasis [21], all established hallmarks of aging. Some authors consider transcriptional noise to be a hallmark of aging in and of itself [22]. In any case, the origin of transcriptional noise is unclear, as it could arise from many different sources. Most importantly, it not possible to distinguish between intrinsic and extrinsic noise from a snapshot of cellular states, i.e., one cannot tell whether the observed differences between cells in a single-cell RNA experiment reflect time-dependent variations in gene expression or differences between cells across a population [23]. Interestingly, recent work by Liu et al. measuring intrinsic noise in S. cerevisiae showed that aging is associated with a steady decrease in noise, with a sudden increase in soon-to-die cells. Another longitudinal study found an increase extrinsic noise and a lack of change in intrinsic noise in diploid yeast [16]."

Regarding the caveat of cells of individuals in the Young groups showing signs of aging, we can only agree that this is correct: there will be cells sampled that already show signs of cellular damage in the absence of chronological aging. However this applies to every study of aging that samples cells in a destructive manner and it is generally assumed by the field that this is a discrete phenomenon that does not affect the overall results in a meaningful way.

3) Another weakness of this study is that the authors did not show the source/cause of decreasing/stable/increasing noise during aging. Understanding the source of loss of cell type identity is also important but this manuscript was about noise in aging, so it would have been nice if there could be some attempts to explain why noise is having this/that trend in differentially aged cell types in specific tissues.

The reviewer raises here a very important point that we would like to discuss in detail. The papers that we have re-analyzed generally assume that an increase in transcriptional noise and a loss in cell type identity are equivalent terms. However, as this reviewer points out, you could theoretically have cells that lose their cell type identity without a concomitant increase in transcriptional noise, for instance by a sharp decrease in a limited number of marker genes that collectively define that cell within a given cell type/cluster. Thus, transcriptional noise can certainly arise from different sources and several mechanisms have been proposed to explain its presence in the context of cellular aging. We agree with the reviewer that discussing how transcriptional noise could be related to aging is of interest to the readers. However, as pointed out in the responses to similar concerns by the other reviewers, our main finding is that we don’t detect meaningful and reliable increases in transcriptional noise associated with cell aging. Instead, what we see is a number of different technical and biological issues/phenomena that have been interpreted as transcriptional noise. We hope this reviewer will agree that the manuscript now presents a full and robust story and that finding the causes of up/down ”noise” trends in the different datasets may be more appropriately tackled by follow up studies.

4) In the discussion section, the authors say that ”Most importantly, Scallop measures transcriptional noise by membership to cell type-specific clusters which is a re-definition of the original formulation of noise by Raser and O’Shea.” It is not clear what the authors refer to by ”the original formulation of noise by Raser and O’Shea”. Intrinsic/extrinsic noise formulations?? Please be more specific.

We thank the reviewer for pointing this out, since we agree that the sentence needed to be reformulated for the sake of clarity. What we meant by the definition by Raser and O’Shea was ”the measured level of variation in gene expression among cells supposed to be identical”, which does not make any distinction between intrinsic and extrinsic noise. Since their definition is previous to the development of single-cell technologies, we meant to state our attempt to bring this classic concept to the context of single-cell RNAseq. Nowadays, cell clusters produced by a community detection algorithm are given cell type annotations depending on their expression of known cell type markers. What Scallop aims to measure is the extent of membership each individual cell has for their cluster as evidence of its transcriptional stability. In order to make this point more clear, we have now rewritten the paragraph as follows:

Most importantly, Scallop measures transcriptional noise by membership to cell type-specific clusters which is a re-definition of the original formulation of noise by Raser and O’Shea: measurable variation among cells that should share the same transcriptome. This is in stark contrast to measurements of noise including other phenomena (as demonstrated in Figure 5) by the distance-to-centroid methods prevalent in the literature.

References

[1] M. Alex Ascensión, Olga Ibáñez-Solé, Iñaki Inza, Ander Izeta, and Marcos J Araúzo-Bravo. Triku: A feature selection method based on nearest neighbors for single-cell data. GigaScience, 11, 2022. doi: 10.1093/gigascience/giac017.

[2] M. Ximerakis, S. L. Lipnick, B. T. Innes, S. K. Simmons, X. Adiconis, D. Dionne, B. A. Mayweather, L. Nguyen, Z. Niziolek, C. Ozek, V. L. Butty, R. Isserlin, S. M. Buchanan, S. S. Levine, A. Regev, G. D. Bader, J. Z. Levin, and L. L. Rubin. Single-cell transcriptomic profiling of the aging mouse brain. Nat Neurosci, 22(10), 2019. doi: https://doi:10.1038/s41593-019-0491-3.

[3] M. Enge, H. E. Arda, M. Mignardi, J. Beausang, R. Bottino, S. K. Kim, and S. R. Quake. Single-cell analysis of human pancreas reveals transcriptional signatures of aging and somatic mutation patterns. Cell, 171(2), 2017. doi: https://doi:10.1016/j.cell.2017.09.004.

[4] L. Solé-Boldo, G. Raddatz, and S. et al. Schütz. Single-cell transcriptomes of the human skin reveal age-related loss of fibroblast priming. Commun Biol, 3(188), 2020. doi: https://doi.org/10.1038/ s42003-020-0922-4.

[5] Jaime L. Schneider, Jared H. Rowe, Carolina Garcia-de Alba, Carla F. Kim, Arlene H. Sharpe, and Marcia C. Haigis. The aging lung: Physiology, disease, and immunity. Cell, 184(8):1990–2019, 2021. doi: 10.1016/j.cell.2021.03.005.

[6] Shuai Ma, Shuhui Sun, Jiaming Li, Yanling Fan, Jing Qu, Liang Sun, Si Wang, Yiyuan Zhang, Shanshan Yang, Zunpeng Liu, and et al. Single-cell transcriptomic atlas of primate cardiopulmonary aging. Cell Research, 31(4):415–432, 2020. doi: 10.1038/s41422-020-00412-6.

[7] I. Angelidis, L. M. Simon, and I. E. et al. Fernandez. An atlas of the aging lung mapped by single cell transcriptomics and deep tissue proteomics. Nature Communications, 2019. doi: https://doi.org/10. 1038/s41467-019-08831-9.

[8] Jonathan M. Raser and Erin K. O’Shea. Noise in gene expression: origins, consequences, and control. Science, 309(5743):2010–2013, 2005. doi: 10.1126/science.1105891.

[9] Michael B. Elowitz, Arnold J. Levine, Eric D. Siggia, and Peter S. Swain. Stochastic gene expression in a single cell. Science, 297:1183– 1186, 2002. doi: 10.1126/science.1070919.

[10] Peter S. Swain, Michael B. Elowitz, and Eric D. Siggia. Intrinsic and extrinsic contributions to stochasticity in gene expression. Proc Natl Acad Sci U S A., 99:12795–12800, 2002. doi: 10.1073/pnas.162041399.

[11] Alex Cagan, Adrian Baez-Ortega, Natalia Brzozowska, Federico Abascal, Tim H. H. Coorens, Mathijs A. Sanders, Andrew R. J. Lawson, Luke M. R. Harvey, Shriram Bhosle, David Jones, Raul E. Alcantara, Timothy M. Butler, Yvette Hooks, Kirsty Roberts, Elizabeth Anderson, Sharna Lunn, Edmund Flach, Simon Spiro, Inez Januszczak, Ethan Wrigglesworth, Hannah Jenkins, Tilly Dallas, Nic Masters, Matthew W. Perkins, Robert Deaville, Megan Druce, Ruzhica Bogeska, Michael D. Milsom, Björn Neumann, Frank Gorman, Fernando Constantino-Casas, Laura Peachey, Diana Bochynska, Ewan St. John Smith, Moritz Gerstung, Peter J. Campbell, Elizabeth P. Murchison, Michael R. Stratton, and Iñigo Martincorena. Somatic mutation rates scale with lifespan across mammals. Nature, 604: 517–524, 2022. doi: 10.1038/s41586-022-04618-z.

[12] Hamit Izgi, Dingding Han, Ulas Isildak, Shuyun Huang, Ece Kocabiyik, Philipp Khaitovich, Mehmet Somel, and Handan Melike Dönertas. Inter-tissue convergence of gene expression during ageing suggests age-related loss of tissue and cellular identity. eLife, 11, 2022. doi: 10.7554/eLife.68048.

[13] Vincent D Blondel, Jean-Loup Guillaume, Renaud Lambiotte, and Etienne Lefebvre. Fast unfolding of communities in large networks. Journal of Statistical Mechanics: Theory and Experiment, 2008(10): P10008, oct 2008. doi: 10.1088/1742-5468/2008/10/p10008. URL https://doi.org/10.1088/ 1742-5468/2008/10/p10008.

[14] V. A. Traag, L. Waltman, and N. J. van Eck. From louvain to leiden: guaranteeing well-connected communities. Scientific Reports, 9, 2019. doi: https://doi.org/10.1038/s41598-019-41695-z.

[15] Peng Qiu. Embracing the dropouts in single-cell rna-seq analysis. Nature Communications, 11(1), 2020. doi: 10.1038/s41467-020-14976-9.

[16] Ethan A. Sarnoski, Ruijie Song, Ege Ertekin, Noelle Koonce, and Murat Acar. Fundamental characteristics of single-cell aging in diploid yeast. iScience, 7:96–109, 2018. doi: 10.1016/j.isci.2018.08.011.

[17] Ping Liu, Ruijie Song, Gregory L. Elison, Weilin Peng, and Murat Acar. Noise reduction as an emergent property of single-cell aging. Nature Communications, 8(1), 2017. doi: 10.1038/s41467-017-00752-9.

[18] Jan Vijg. From dna damage to mutations: All roads lead to aging. Ageing Res Rev., 68(101316), 2021. doi: 10.1016/j.arr.2021.101316.

[19] Yuancheng Lu, Benedikt Brommer, Xiao Tian, Anitha Krishnan, Margarita Meer, Chen Wang, Daniel L. Vera, Qiurui Zeng, Doudou Yu, Michael S. Bonkowski, Jae-Hyun Yang, Songlin Zhou, Emma M. Hoffmann, Margarete M. Karg, Michael B. Schultz, Alice E. Kane, Noah Davidsohn, Ekaterina Korobkina, Karolina Chwalek, Luis A. Rajman, George M. Church, Konrad Hochedlinger, Vadim N. Gladyshev, Steve Horvath, Morgan E. Levine, Meredith S. Gregory-Ksander, Bruce R. Ksander, Zhigang He, and David A. Sinclair. Reprogramming to recover youthful epigenetic information and restore vision. Nature, 588(7836):124–129, 2020. doi: 10.1038/s41586-020-2975-4.

[20] Giorgio Oliviero, Sergey Kovalchuk, Adelina Rogowska-Wrzesinska, Veit Schwämmle, and Ole N. Jensen. Distinct and diverse chromatin proteomes of ageing mouse organs reveal protein signatures that correlate with physiological functions. eLife, 11(e73524), 2022. doi: 10.7554/eLife.73524.

[21] Jingyi Li, Yuxuan Zheng, Pengze Yan, Moshi Song, Si Wang, Liang Sun, Zunpeng Liu, Shuai Ma, Juan Carlos Izpisua Belmonte, Piu Chan, Qi Zhou, Weiqi Zhang, Guang-Hui Liu, Fuchou Tang, and Jing Qu. A single-cell transcriptomic atlas of primate pancreatic islet aging. Natl Sci Rev., 8(2): nwaa127, 2020. doi: 10.1093/nsr/nwaa127.

[22] Alexander R. Mendenhall, George M. Martin, Matt Kaeberlein, and Rozalyn M. Anderson. Cellto-cell variation in gene expression and the aging process. Geroscience, 43(1):181–196, 2021. doi: 10.1007/s11357-021-00339-9.

[23] Lucy Ham, Marcel Jackson, and Michael PH Stumpf. Pathway dynamics can delineate the sources of transcriptional noise in gene expression. eLife, 10, 2021. doi: 10.7554/elife.69324.

Author Response

Reviewer #1 (Public Review):

This work identifies distinct contribution of direct (D1+) and indirect (Adora+, D2+) amygdalostriatal medium spiny cells in fear learning and plasticity. The authors combined freely moving calcium imaging with auditory fear learning assay to reveal tone, foot-shock and behavior (movement)-evoked activity of the two MSN population. While D1+ cells show plastic changes driven by fear learning and reaching their maximum tone responsiveness (PSTH) at fear retrieval, Adore+ cells activation remained constant. Furthermore, using optogenetic silencing they showed that the two MSN groups differently contribute to retrieval of fear memory. Both cells receive topographically organized insular cortical inputs which go through learning-induced long-term synaptic changes with opposite direction: postsynaptic LTP at D1 cells, while presynaptic LTD at Adora+ cells. These synaptic changes provide some level of explanation for distinct behavioral contribution of the two cell types in fear learning.

This study focuses on a so far neglected member of the 'extended' amygdalar circuitry, the amygdalostratal transition zone. The data is well-presented, the experiments are in logical order, built on each other and the paper is easy to read and follow.

However, some information regarding the connectivity (and function) of Astr have been presented in recent and earlier papers are missing from, or contradicting with, the present work. One reason to explain these is that the targeted striatal regions vary between experiments, and so, it is difficult to judge when the Astr and when the other part of the caudal (tail) striatum is examined. As these striatal regions are involved in different neuronal networks, their functional consequences could also be distinct. Without precisely clarifying and consistently targeting the aimed striatal region, it is difficult to interpret the findings of the present study (though those are relevant and important).

We thank this reviewer for his/her overall positive evaluation of our paper.

We agree with the criticism that in the first submission, we have not stringently defined the anatomical region of the amygdala - striatal transition zone (AStria). After validating our previous data, and after performing new anatomical experiments studying the expression of Cre in the D1RCre and AdoraCre mouse lines used here (see Figure 1D; Figure 1 - figure supplement 1; Figure 3 - figure supplement 1), we now refer to the region targeted in our study as "ventral tail striatum" (vTS), as opposed to the more narrowly defined, and more ventrally located "AStria". Therefore, we have changed the word "AStria" to ventral tail striatum ("vTS") throughout the paper.

We have also improved our introduction to the posterior striatum (p. 4 bottom, p. 5 top), and we briefly discuss the targeting of the vTS (as opposed to the AStria)(p. 19 top).

Reviewer #2 (Public Review):

Kintscher et al present a nice study on the responses of Adora2a and D1R expressing cells in the tail of the striatum/amygdala transition zone during auditory fear conditioning. Overall the conclusions are that (1) D1R cells show plasticity in activity patterns during the task, with the emergence of tone/movement co-modulated cells; (2) Adora2a cells show less of such changes; (3) gain of function of activity does little where (4) loss of function of activity in each cell class has moderate effects on the learned behavior (i.e. freezing to the CS). There is a nice section on rabies tracing which maps inputs to both cell types which then motivates an analysis of insular cortex inputs onto both cell types and reveals that (5) CS/US pairing alters insular inputs to both cell types.

Overall the paper is well done and the conclusions are believable. Furthermore, this brain area is understudied yet potentially very important.

The analysis of the fluorescence transients is heavy handed. This leads to potential for error and could obscure what appear to be large differences that could be extracted more easily. In some instances, the data are interpreted too optimistically, especially that the silencing experiments implicate plasticity of the neurons rather than the need for activity.

We thank the reviewer for his/her positive evaluation of our paper. For the revision, we have re-analyzed the Ca-imaging data, and we have made changes in the text to avoid a too optimistic interpretation of our data.

Author Response

Reviewer #2 (Public Review):

Wild and colleagues develop a barcoding approach, termed WILD-seq, that combines tumor cell barcoding with single cell transcriptional analysis to concurrently examine clonal tumor cell dynamics and cell state changes during drug treatment. They examine two triple-negative breast cancer (TNBC) cell lines in vivo in response to JQ1 and taxanes. Results from these experiments yield several meaningful conclusions. First, they demonstrate that clonal dynamics are fundamentally distinct depend ending on context and microenvironment, with significant differences observable between cell culture, NSG and immunocompetent mice. Second, they show that bulk expression in treatment refractory tumors represents clonal outgrowth of subpopulations in pretreatment tumors that bear gene expression patterns similar to the tumor relapsed. Finally, they identify mechanisms of in vivo taxman resistance, including EMT and high NRF2 expression - the latter yielding tumors that show collateral sensitivity to L-asparaginase and subsequent resistance mediated by high levels of asparagine synthetase.

This study is a technical tour de force. The authors deeply engage the complexity of cell barcoding, bottle necking, Hamming analysis, single cell expression analysis and microenvironmental cell analysis. The idea that bulk tumor expression states demarcate drug resistant clonal populations in pre-treatment tumors, while not a new concept, finds critical validation using this approach. Moreover, the use of this approach to examine collateral sensitivity and to identify new strategies to target taxane resistance is compelling.

I support this work but might suggest some comparisons of primary and relapse tumors, as well as the nature of the taxane collateral sensitivity, be further extended.

Major comments:

1) The authors suggest that the bulk expression analysis in relapsed tumors mirrors clonal populations in pretreatment tumors (which, while requiring barcoding to validate, somewhat obviates the need for barcoding to identify mechanisms of drug resistance). In cases like EMT, it has been argued that mesenchymal tumor cells survive therapy, but then undergo MET in the relapsed state. Thus, in the long term, tumors may revert to pre-treatment clonal states. It would be interesting to see whether that is the case here - and whether the informative nature of bulk gene expression in the drug resistant tumor is lost over time.

This is an interesting point. We don’t have any direct evidence of any of the tumour cell lineages in our model undergoing EMT or MET from our work, but it is entirely possible that the tumour cells dynamically transition between states over longer time frames that we haven’t captured in our experiments to date. It is also possible that there are intermediate states that we have not captured by sampling at end-point. WILD-seq presents an excellent method for such studies but these are beyond the scope of the current paper.

For such experiments, it would be essential to use barcoded cells to track clonal lineage, otherwise it is impossible to determine whether changes in the EMT of a tumour cell population was driven by a change in the transcriptome/cell state or a shift in clonal abundance. We have added discussion of these points to the discussion section of the manuscript.

With respect to the necessity of barcoding for identifying treatment resistance mechanisms over bulk approaches, lineage-based analysis serves to prioritise pathways that change in the resistance setting that might otherwise be overlooked as being lower down the list of differential expression in bulk analysis. While not specifically addressed here, being able to differentiate between a pre-existing resistance phenotype or an adaptive mechanism of resistance, may also inform the choice of dosing schedule of agents targeting resistant clones.

2) Collateral resistance can either refer to the outgrowth of clones that show enhanced sensitivity to distinct therapies or the therapeutic induction of cell states that respond differently to other drugs. To confirm that L-asparaginase sensitivity results from the specific outgrowth of NRF2 clones, it would be meaningful to show that these clones are lost upon L-asparaginase-only treatment and that pretreatment of L-asparaginase promotes long term efficacy of taxanes.

We agree this is a critical question and one that we had already started to address while the manuscript was under review. The Nrf2-high clones are lowly represented in vehicle treated tumours and on the edge of our detection threshold, thus accurate measurements of their depletion by L-asparaginase-only treatment in tumours derived from our heterogeneous WILD-seq clonal pools is very challenging. To address this question, we have instead chosen to isolate individual resistant clones and directly test their response to L-asparaginase. We were able to isolate two of the Nrf2-high clones (751 and 1240) by growing up clones from single cells. After expansion in vitro, these were implanted as pure monoclonal populations and the resulting tumours treated with L-asparaginase. These new data, presented in Fig 7g, demonstrate that tumours derived from these clones (in contrast to tumours derived from our WILD-seq pools) significantly respond to L-asparaginase-only treatment, suggesting that this cell state is a pre-existing intrinsic property of these clones and not one induced by docetaxel treatment.

Author Response

Reviewer #1 (Public Review):

It has been shown that selenium protects against the development of epilepsy, and behavioral comorbidities, as pointed out by the authors. This paper attempts to show it does if administered later after chronic seizures start. While clinically relevant, as noted by the authors, the paper seems not to be a major advance beyond the prior study. The antiseizure effect is also not very convincing because the effect size is so small and the variance so high. The data about behavior is more convincing but similar data were in the previous paper, so it is not very novel.

Thank you for reviewing our paper. Previous work has shown that sodium selenate, not selenium, can delay the appearance of seizures and mitigate behavioural comorbidities if given immediately after the epileptogenic brain insult, but before the appearance of spontaneous recurring seizures (i.e. before epilepsy development), i.e. is anti-epileptogenic. The novelty of our current work is that we are treating once epilepsy develops, i.e. is disease-modifying. This is the first time a pharmacological agent has been shown to be disease-modifying in established epilepsy, resulting in an enduring reduction in seizures suppression even after treatment withdrawal, as well as to mitigate the behavioural comorbidities that commonly are co-morbid with chronic epilepsy. This is potentially ground-breaking new findings for the epilepsy field, as at present the only current disease-modifying therapy for established chronic epilepsy is epilepsy surgery.

Author Response

Reviewer #1 (Public Review):

Building upon the previous evidence of activation of auditory cortex VIP interneurons in response to non-classical stimuli like reward and punishment, Szadai et al., extended the investigation to multiple cortical regions. Use of three-dimensional acousto-optical two-photon microscopy along with the 3D chessboard scanning method allowed high-speed signal acquisition from numerous VIP interneurons in a large brain volume. Additionally, activity of VIP interneurons in deep cortical regions was obtained using fiber photometry. With the help of these two imaging methods authors were able to extract and analyze the VIP cell signal from different cortical regions. Study of VIP interneuron activity during an auditory go-no-go task revealed that more than half of recorded cortical VIP interneurons were responding to both reward and punishment with high reliability. Fiber photometry data revealed similar observations; however, the temporal dynamics of reinforcement stimuli-related response in mPFC was slower than in the auditory cortex. The authors performed detailed analysis of individual cell activity dynamics, which revealed five categories of VIP cells based on their temporal profiles. Further, animals with higher performance on the discrimination task showed stronger VIP responses to 'go trials' possibly suggesting the role of VIP interneurons in discrimination learning. Authors found that reinforcement related response of VIP interneurons in visual cortex was not correlated with their sensory tuning, unveiling an interesting idea that VIP interneurons take part in both local as well as global processing. These observations bring attention to the possible involvement of VIP interneurons in reinforcement stimuli-associated global signaling that would regulate local connectivity and information processing leading to learning.

The state-of-the-art imaging technique allowed authors to succeed in imaging VIP interneurons from several cortical regions. Advanced analyses revealed the nuances, similarities and differences in the VIP activity trend in various regions. The conclusions about reinforcement stimuli related activity of VIP interneurons made by the authors are well supported by the results obtained, however some claims and interpretations require more attention and clarification.

We thank Reviewer #1 for the positive general comments.

Reviewer #2 (Public Review):

In recent years the activity of cortical VIP+ interneurons in relation to learning and sensory processing has raised great interest and has been intensely investigated. The ability of VIP+ interneurons in the auditory cortex to respond to both reward and punishment was already reported a few years ago by some of the authors (Pi et al., 2013, Nature). However, this work importantly adds to their previous study demonstrating a largely similar and synchronous response of a large fraction of these interneurons across the neocortex to salient stimuli of different valence during the performance of an auditory discrimination task.

An additional strength of this study is the analysis and identification of the general pattern of VIP+ interneuron responses associated to specific behaviors in the different layers of the neocortex depth.

Interestingly, the authors also identified using cluster analysis 5 different classes of VIP+ interneurons, based on the dynamic of their responses, that were unequally distributed in distinct cortical areas.

This is a well performed study that took advantage of a cutting-edge imaging approach with high recording speed and good signal-to-noise ratio. Experiments are well performed and the data are properly analyzed and nicely illustrated. However, one shortcoming of this paper, in my opinion, is the "case report" structure of the data. Essentially for each neocortical area the activity of VIP+ interneurons was analyzed only in one animal. This limits the assessment of the stability of the response/recruitment of these interneurons. I appreciate the high number of recorded VIP+ interneurons per area/animal and I do understand that it would be excessively laborious to perform 3D random-access two-photon microscopy in several mice for each cortical area. On the other hand, it would be important to have some knowledge of the general variability of the responses of these neurons among animals.

In conclusion, despite the findings described in this manuscript being generally sound, additional experiments are recommended to further substantiate the conclusions.

Thank you for pointing out this potential misunderstanding. Although we mentioned the number of animals the recordings were obtained from (n=22 total), we repeated this multiple times to alleviate the potential confusion. The data recorded with the 2-photon microscope are from 16 animals, and fiber photometry was performed on a separate 6 animals. Each animal was recorded in one (14 mice) or two areas (8 mice, 2 AOD, 6 photometry). We aimed to acquire data from at least 3 recordings per area (4 in the primary somatosensory cortex, 6 in the primary and secondary motor cortices, 4 in the lateral and medial parietal cortices, 3 in the primary visual cortices, 6 in the auditory and medial prefrontal cortices). In the revised manuscript this information can be found at the beginning of the results section and in the figure legends:

“To probe the behavioral function of VIP interneurons, we trained head-fixed mice (n=22 in total, n=16 for 2-photon microscopy and n=6 for fiber photometry) on a simple auditory discrimination task (Figure 1A).”

“Among the 811 neurons imaged in 18 imaging sessions from 16 mice,”

“Ca2+ responses of individual VIP interneurons recorded separately from 18 different cortical regions from 16 mice using fast 3D AO imaging were averaged for Hit (thick green), FA (thick red), Miss (dark blue), and CR (light blue). Fiber photometry data were recorded simultaneously from mPFC and ACx regions and are shown in gray boxes. Functional map (Kirkcaldie, 2012) used with the permission of the author. Speaker symbols represent the average time of tone onset, and gray triangles mark the reinforcement onset for Hit and FA. Averages of Miss and CR trials were aligned according to the expected reinforcement delivery calculated on the basis of the average reaction time. mPFC: medial prefrontal cortex (n=6 mice), ACx: auditory cortex (n=6), S1Hl/S1Tr/S1Bf/S1Sh: primary somatosensory cortex, hindlimb/trunk/barrel field/shoulder region (n=4), M1/M2: primary/secondary motor cortex (n=6), Mpta/Lpta: medial/lateral parietal cortex (n=4), V1: primary visual cortex (n=3).”

“This approach allowed us to simultaneously measure bulk calcium-dependent signals from VIP interneurons located in the right medial prefrontal (mPFC) and left auditory cortices (ACx) by implanting two 400 µm optical fibers at these locations (n=6 sessions from n=6 mice, Figure 1–figure supplement 1C).”

“Raster plot of the trial-to-trial activation of the responsive VIP neurons in Hit and FA trials during the two-photon imaging sessions (n=18 sessions, n=16 mice, n=746 cells).”

Subregional labels, for example on Figure 2, should be considered as additional information to orient the readers, even if they were very precisely defined on the basis of the coordinates. All analyses considering regional differences were conducted on the level of the main functional areas of the dorsal cortex (motor, somatosensory, parietal, and visual). Despite some location-dependent heterogeneity in the late response phase (Figures 2G and H), even these main dorsal cortical regions were all similar from the perspective of responsiveness to reinforcers and auditory cues.

Reviewer #3 (Public Review):

In this study Szadai et al. show reliable, relatively synchronous activation of VIP neurons across different areas of dorsal cortex in response to reward and punishment of mice performing an auditory discrimination task. The authors use both a relatively fast 2 photon imaging, as well as fiber photometry for some deeper areas. They cluster neurons according to their temporal response profiles and show that these profiles differ across areas and cortical depths. Task performance, running behavior and arousal are all related to VIP response magnitude, as has been previously shown.

Methodologically, this paper is strong: the described imaging technique allows for fairly fast sampling rates, they sample VIP cells from many different areas and the analyses are sophisticated and touch on the most relevant points. The figures are of high quality.

However, as the manuscript is now, the presentation could be clearer, the methods more complete and it is not clear whether their conclusions are entirely supported by the data.

The main issue is that reinforcement and arousal are hard to distinguish in this study. It is well known that VIP activity is correlated with arousal. And it is fairly clear that the reinforcement they use in this study - air puffs to the eye, as well as water rewards - cause arousal. It is possible that the reinforcer responses they observe in VIP neurons throughout all areas merely reflect the increases in arousal caused by these behaviorally salient events. They do discuss this caveat (albeit not fully convincingly) and in their abstract even state that the arousal state was not predictive of reinforcer responses. However their data clearly shows the tight relationship of the VIP reinforcer responses to both arousal (as measured by pupil diameter), as well as running speed of the animal. Both of these variables are well known to be tightly coupled to VIP activity.

Although barely mentioned, the authors do appear to sometimes present uncued reward (Figure S2F). If responses were noticeably different from the same events in the task context (as actual reinforcers) this could at least hint towards the reinforcement signal being distinct from mere arousal. However, this data is only mentioned in one supplementary figure in a different context (comparison with PV cells) and neither directly compared to cued reward, nor is this discussed at all. Were uncued air puffs also presented? How do the responses compare to cued air puffs/punishment?

Our original approach to distinguish between reinforcement- and arousal-related responses aimed:

1) to show that VIP cells with both low and high correlation coefficients with arousal produce large signals upon reinforcement presentation (Figure 3B),

2) the high differences of low and high arousal changes were reflected in a limited way in the VIP activity (Figures 3C and D): as highlighted in Figure R1, where we also added bars to show ∆P/P in high and low pupil change conditions, the difference in ∆P/P is ~5-fold, while it is only ~1.5-fold for ∆F/F. This disproportionality suggests that a large part of the signal below the dashed blue line is independent of arousal. We have added these modifications to the new version of Figure 3 for clarity.

Figure R1 = Figure 3C-D with modification. Comparison of pupil changes and corresponding calcium averages.

We collected further evidence to support our claims. In Figure 3–figure supplement 2 we depicted Hit and FA trials in which the reinforcement didn’t elevate the arousal level any further. Many of these trials were associated with locomotion prior to the reinforcement, but it was also common that the animals remained still during the whole trial. Trials with increased locomotion upon reinforcement presentation were excluded. Reinforcement-related calcium signals were still present under these conditions, indicating that these signals are not simple reflections of arousal. Moreover, we estimate the distinct contributions of arousal, locomotion, and reinforcers in Figure 3–figure supplement 2D in a systematic way with a generalized linear model. This model also confirmed our view about the reinforcement-related coding.

We now say in the results:

“Finally, to assess the motor- and reinforcement-related contributions to VIP interneuronal activity, we built a generalized linear model using the behavior and imaging data of the SS and Mtr recordings (Figure 3–figure supplement 2D, n=3 mice). This model was able to explain 18.8 ± 11.1% of the variance of the VIP population calcium signal, and highlighted that arousal was the best predictor, followed by reward, punishment, locomotion velocity, and auditory cue (weights = 0.055, 0.031, 0.028, 0.020, 0.018 respectively; all predictors, except the auditory cue in the case of one animal, contributed significantly, p<0.001). These observations indicate that running and arousal changes alone cannot fully explain the recruitment of VIP interneurons by reinforcers.”

We apologize for not describing the rational and the result from the uncued reward experiments. Briefly, while recording reinforcement related signals in auditory cortex in our task, we realized that the cue delivery, and the resulting purely sensory response could alter the measurement of the reward-related responses. Hence, in order to disentangle the reward and sensory-related responses, we presented the animals with simple, uncued reward and observed a similar and robust recruitment of VIP interneurons. Based on the same rational, we made similar measurement for PV neurons.

We now say in the results:

“We did not further analyze the FA responses in auditory cortex as those responses also had a sensory component linked to the white noise-like sound created by the air puff delivery. Because the cue delivery could prove as a confound to measure reward-mediated responses from VIP interneurons in auditory cortex (see also methods), we delivered random reward in separate sessions. Water droplets delivery recruited VIP interneurons in both auditory and medial prefrontal cortex in a similar fashion as water delivery during the discrimination task (Figure 2–figure supplement 1G). Like our single cell results, PV-expressing neuronal population in ACx did not show any significant change in activity upon similar random reward delivery (Figure 2–figure supplement 1G).”

Regarding the difference between cued and uncued responses, we definitely agree with the reviewer that it is an important point. The goal of this manuscript is however to study how reward and punishment are being represented by VIP interneurons in cortex.

The imaging method appears well suited for their task, however the improvements listed in table S1 make the method appear far superior to existing methods in many aspects. Published or preprinted papers with 2 photon imaging of VIP populations (eg. from Scanziani lab (Keller et al.), Carandini lab (Dipoppa et al.), deVries lab (Millman et al.), Adesnik lab (Mossing et al.), which use the much more common resonant scanning, seem to be able to image 4-7 layers at 4-8Hz with a good enough SNR and potentially bigger neuronal yield of approximately 100-200 VIP cells, depending on the field of view. While not every single cell in a volume would be captured by these studies, the only main advantage of the here-used technique appears to be the superior temporal resolution.

We thank the reviewer for the positive comment and we agree that interpretation must be improved. We agree that the imaging methods in the papers listed above have good SNR and were proper to address the scientific questions that had arisen. As the reviewer points out, 3D-AOD imaging allows fast 3D measurement that cannot be achieved otherwise. We used these advantages to address the critical question of layer specificity in the response of VIP interneurons to reinforcer presentation (Figure 2–figure supplement 1F, but see also the new Figure 1–figure supplement 1B). Regarding the comparison and quantification of the factual advantages of AOD microscopy over other imaging methods, the reviewer and readers can refer to the methods section (3D AO microscopy), Table S1 and Szalay et al., 2016. We agree with the reviewer that one of the main advantages is the superior temporal resolution. The second main advantage is the improved SNR. This originates from the fact that the entire measurement time is spent on regions of interest; measurement of unnecessary background areas is not required. More specifically, SNR is improved even in the case of 2D imaging by the factor of:

((area of the entire frame )/(area of the recorded VIP cells))^0.5

which is about (100)0.5=10 as VIP interneurons represent about 1% of the brain. We used this second advantage of AO scanning when we determined the activation ratio (e.g., see Figure 2D).

As the resolution of single or a few action potentials is challenging in behaving mice labelled with the GCaMP6 sensor, any improvement in SNR will improve the detection threshold. The higher SNR achieved here improved the detection threshold, which also explains the relatively high activation ratio in our work.

In the case of asynchronous activity patterns, there is negligible contribution of individual small neuropil structures to somatic activities because of the relatively high volume-ratio of a soma and a given small neuropil structure: this minimizes the error during ∆F/F calculation of somatic responses. However, reinforcement, arousal, and running can generate highly synchronous neuronal activities which can synchronize neuropil activity around a given soma and, therefore, effectively and systematically modulating the somatic ∆F/F responses. To avoid this error, we used a high NA objective with proper neuropil resolution and combined it with motion correction. The use of the high NA also decreased the total scanning volume to about 689 µm × 639 µm × 580 µm and, therefore, it limited the maximum number of VIP cells which could be recorded. It is also possible to use a low-NA objective with a much higher FOV and scanning volume and record over 1000 VIP cells, but the extension of the PSF along the z dimension is inversely and quadratically proportional to the NA of the objective, therefore neuropil resolution will be at least partially lost. In summary, using the high-NA Olympus objective we maximized the 2P resolution which, in combination with off-line motion artifact elimination, allowed precise recording of somatic signals without any neuropil contamination: this provided correct activation ratio values.

Even though this is not mentioned at all, it certainly appears possible, that the accousto-optical scanning emits audible noise. In this case it would be good to know the frequency range and level of this background noise, whether there are auditory responses to the scanning itself and if it interferes with the performance of the animals in the auditory task in any way. If this is not the case, this should probably simply be mentioned for non-experts.

While the name of the acousto-optical deflectors seems to refer to “acoustic noise”, these devices are driven in the range of 55-120 MHz, which is 3 orders of magnitude higher frequency than the hearing threshold of animals: mice don’t hear them. Moreover, we developed water-cooled AODs ten years ago which means that ventilators are also not required, therefore AOD-based scanning can be used with zero noise emission. In contrast, galvo, resonant, and piezo scanning work in the kHz frequency range, which is in the middle of the hearing range of mice. Moreover, these technologies can’t be used in a vacuum and the scanner is just a few tens of centimeters away from the mice, which means that acoustic noise can’t be canceled but can only be partially suppressed with white noise. We thank the reviewer for the helpful comment and have added one sentence about the absence of acoustic noise during acousto-optical scanning:

“The deflectors are driven in the 55-120 MHz frequency range, therefore the noise emitted does not interfere with the auditory cues, as mice can’t hear it. This, in combination with the water cooling of the deflectors, makes the AOD-based scanning the quietest technology for in-vivo imaging.”

The authors show a strong correlation between task performance (hit rate) and the response to the auditory cue on hit trials. Was there any other significant correlations of VIP cells' responses to other trial types? Was reinforcer response correlated to behavioral variables at all?

We have not found any remarkable correlations between VIP cell activity and behavioral variables except the one mentioned above.

For example, we tested discrimination rate (hit rate/FA rate) correlation with ∆F/Ftone in Hit trials, but this was not significant (R2=0.03, F=0.49, p=0.69), just like Hit rate vs. ∆F/Ftone in FA trials (R2=0.19, F=3.8, p=0.07), and discrimination rate vs. ∆F/Ftone in FA trials (R2=0.07, F=1.1, p=0.31).

Author Response

Reviewer #1 (Public Review):

“Even though the methodology was already introduced, it should be described in some detail. Most importantly, AlphAfold's measures of accuracy have been part of the loss function during training/testing. What about the measure of protein-protein interaction accuracy? Was it also in the loss function?”

We thank the reviewer for this insightful comment. The metrics used for evaluating predicted structure quality, such as the predicted local distance difference test (pLDDT) score and predicted TM score (pTM), both proposed in the AlphaFold 2 publication (Ref. 27), and the interface score (iScore) proposed in the AF2Complex publication (Ref. 23), are not explicitly employed as the loss function in training the main deep learning model for structure prediction. Instead, the main loss function of AF2 is the Frame Aligned Point Error (FAPE) loss, which measures the errors in the predicted atomic coordinates within local coordinate frames spanned by vectors connecting backbone heavy atoms of individual protein residues. However, this FAPE loss function is very much relevant to predicting TM-scores or iScores; both are derived from an additional module that predicts alignment errors (PAEs) viewed from each residue’s local frame. The training of this PAE module was done separately as described in the AF2 publication (Ref. 27). According to DeepMind, the training of the deep learning models for AlphaFold-Multimer (Ref. 25, AF version 2.2.0 and above) has relatively minor changes in the loss function; changes were made mainly to reduce severe clashes, which were not uncommon in modeling large complexes by earlier versions of AF2.

We added in the Methods section, line 337,

“The iScore metric was derived from the predicted alignment errors that gives an estimated distance for interface residue j from its position in the experimental structure, as viewed from a local frame of residue interface residue i [23,27]. To better estimate confidence, the contribution of each interface residue to the interface score is calculated using local frames not located within the same protein chain, i.e., residue i and j belonging to different chains.”

“Figure 1a (upper panel, PpiD) includes quite a few promising hits but only the first, third, and 12th were considered. How were these chosen? For example, why not consider the second? The lower panel (YfgM) also shows many promising hits but only the first was chosen. Why not more? Likewise, only two of the top hits in Figure 4 are considered. What about the rest? For example, why taking into account the second best hit while skipping the first?”

These are important questions about similar issues raised by all three reviewers, i.e., R2.1 by reviewer 2 and R3.2 by reviewer 3. We emphasize that our approach predicts physical interactions between proteins, not the biological consequence of such interactions. However, since the most interesting predictions are the ones relevant to biological functions, about which the computational method cannot make a judgement, given the space limitations of the manuscript, we opted to select from the top predictions those that likely provide mechanistic insights into biological function, for example, those that might inspire new hypotheses about molecular mechanisms. In practice, our selection process was guided by existing literature and experimental evidence. Since such information is limited, we can only focus on the very few ones with both strong computational and experimental evidence. Most top predictions, including the ones the reviewers questioned, were not pursued further because we cannot at present say anything about the functional consequences of these predicted interactions, even though they may interact physically. One main contribution of this computational screening approach is to provide short lists that accelerate the search for functionally important protein-protein interactions. Thus, in this contribution, we provide some examples found in the top 20 hits ranked from ~1500 possible pairs for a given query protein.

In this revision, we added from line 85,

“Note that our computational predictions are about physical interactions between a pair of proteins subjected to screening, not about their biological roles even if they are predicted to interact physically. Moreover, the predicted physical interactions may not be relevant in the cellular environment due to various factors not considered in modeling, e.g., competition from other proteins with stronger binding affinities, post-translational modifications, etc. Thus, it is possible that many protein-protein interactions predicted by this pipeline do not necessarily have biological relevance. Nevertheless, since cognate protein-protein interactions required by their functions are more likely to be detected than randomly selected proteins, biologically interesting protein-protein interactions are enriched at the top of the screening results ranked by iScore. Thus, the screening procedure may provide valuable even critical clues for subsequent investigation. In this study, assisted by existing experimental evidence, we select from high confidence computational predictions those most likely to have significant biological implications, and then predict the structures of larger complexes if more than two proteins are involved according to our predictions or based on literature information. The interactions that we ignored are either of unknown biological significance, physically interacting but biologically irrelevant, or simply false positives.”

“Authors argue that the unstructured part of OmpA, which wraps around SurA, is to be trusted, which may be the case. But a more likely explanation is that it is an artefact, in agreement with the very low confidence assigned by AlphaFold.”

While we do not disagree that the structure prediction about SurA/OmpA complex may contain artifacts, there are several reasons why our predications may be insightful, as we explained in the manuscript. First, it is well-known in experimental studies (references 41, 42, 45) that the SurA/OmpA complex is very dynamic and unlikely to possess a stable structural complex as in a typical crystal structure. As such, the low confidence score by AF2Complex is expected, as it reflects uncertainty due to the existence of many possible conformations. Second, it makes physical sense to have loose wrapping of OmpA around SurA, as it reduces the energetic costs to dissociate OmpA from SurA when SurA approaches BAM for its delivery. Our point is a qualitative assessment, rather than claiming a specific complex model as in a typical structure prediction scenario. To be cautious as the reviewer suggested, we added a sentence in the Discussion, from line 309,

“Despite the low confidence due to weak interactions, the predicted structures delineate a picture for how SurA prevents OmpA from aggregating. Moreover, since it transports OmpA with a relatively small number of intermolecular contacts, the free energy required to dissociate OmpA from SurA is small. Notwithstanding these considerations, we caution that artifacts likely exist in these predicted structural models.”

“Figure 5. How is (does) this predicted structure compare with the known structure of the complex? In particular, how similar are the predicted and known structures of the individual subunits, and how similar are the predicted docking poses to the known ones?”

The BAM complex has been studied extensively, with over one hundred experimental structures of its individual subunits or the full complex. Therefore, a thorough structural comparison is a subject of a review beyond the scope of this study. In our computational models, the structures of the individual subunits or of the full BAM complex closely mimic their known experimental structures, which is expected because some of these structures were likely employed in the training of deep learning models and/or structure predictions. We added a comparison to the highest resolution crystal structure in the revised manuscript after line 225,

“Because BAM has been extensively studied structurally [7,47], we focus on describing its interaction with SurA, though the predicted BAM complex model closely mimics a known crystal structure of the complex determined at 2.9 Å resolution (PDB 5D0O, [48]). The alignment of the two complex structures yields a very high TM-score of 0.94.”

“Authors should make the results easily accessible to all. Maybe as Cytoscape and CyToStruct sessions for easy visualization.”

Cytoscape and the add-on CytoStruct are very useful tools to visualize large networks. In our case, however, we are presenting only a handful of complexes, not a massive protein-protein interaction network like those resulting from all-against-all screening at proteome-scale. A diagram such as Fig. 7 is sufficient for our visualization purposes. Moreover, we provide the atomic coordinates in the standard PDB format for readers who wish to examine the respective structures in detail. In the future, if we have opportunity to expand PPI screening to a large number of targets, Cytoscape and add-ons will be handy to display the resulting gigantic network.

“Finally, AlphaFold was trained and tested mostly with water-soluble protein. Thus, application to outer membrane proteins is a bit risky. Maybe authors can comment on this.”

While it is true that most experimental structures used for training AlphaFold models are of water-soluble proteins, there are also structures of many membrane proteins available for training, as over 10,000 structures of membrane-proteins were already deposited in the Protein Data Bank, though there are redundancy within these structures and some domains are outside the transmembrane regions. These structures are likely sufficient for machine-learning approaches such as AlphaFold 2 to learn the sequence and structural patterns unique to transmembrane proteins. This view is supported by our empirical experience, because transmembrane regions of membrane proteins are typically among those with high confidence scores, e.g., complex models for a transmembrane molecular system CcmI presented in our AF2Complex work (Ref. 23). And one of these computational models (of CcmA2B2CD) was just confirmed to have high quality by cyro-EM models (Li et.al., Nature Communications 13:6422, 2022) at TM-score 0.89. We note that this was a non-trivial prediction as this structure was not present in the PDB and was long sought by the experimentalists. The view also agrees with the conclusion of a recent published study on AF2 models of transmembrane proteins (Hegedűs, et. al. Cell. Mol. Life Sci. 79:73, 2022).

Author Response

Reviewer #1 (Public Review):

The authors present a study of figure-ground segregation in different species. Figure-ground segregation is an important mechanism for the establishment of an accurate 3D model of the environment. The authors examine whether figure-ground segregation occurs in mice in a similar manner to that reported in primates and compare results to two other species (Tree shrews and mouse lemurs). They use both behavioral measures and electrophysiology/twophoton imaging to show that mice and tree shrews do not use opponent motion signals to segregate the visual scene into objects and background whereas mouse lemurs and macaque monkeys do. This information is of great importance for understanding to what extent the rodent visual system is a good model for primate vision and the use of multiple species is highly revealing for understanding the development of figure-ground segregation through evolution.

The behavioral data is of high quality. I would add one caveat: it seems unfair to report that the tree shrews could not generalize the opponent motion stimulus as it seems they struggled to learn it in the first place. Their performance was below 60% on the training data and they weren't trained for many sessions in comparison to the mice. Perhaps with more training the tree-shrews might have attained higher performance on the textures and this would allow a more sensitive test of generalization. The authors should qualify their statements about the treeshrews to reflect this issue.

The reviewer is correct in this assertion. For context, we performed the mouse experiments first and were hoping to see texture-invariant performance but instead realized that the mice were resorting to memorizing patterns. With this in mind, when expanding to treeshrews we wanted to prevent this type of learning to really test whether texture invariant recognition was possible, thus we increased the number of orientations tested to 5, resulting in 10 possible textures that would have to be memorized in contrast to the 4 that had to be memorized for the mice. We now clarify this in the text:

“We reversed the number of train/test patterns compared to what was used for the mice (Fig. 2i1) because we reasoned that animals might be more likely to generalize if given more patterns for training. We had performed the mouse experiments initially, noticed the memorization approach, and were trying to avoid this behavior in treeshrews. This also means that the naturalistic train condition presented to treeshrews was harder than that for mice (5 orientations for treeshrews vs. 2 orientations for mice in the training set).”

Reviewer #2 (Public Review):

Luongo et al. investigated the behavioural ability of 4 different species (macaque, mouse lemur, tree shrew and mouse) to segment figures defined by opponent motion, as well as different visual features from the background. With carefully designed experiments they convincingly make the point that figures that are not defined by textural elements (orientation or phase offsets, thus visible in a still frame) but purely by motion contrast, could not be detected by nonprimate species. Interestingly it appears to be particularly motion contrast, since pure motion - figures moving on a static background - could be discriminated better, at least by mice. This is highly interesting and surprising -- especially for a tree shrew, a diurnal, arboreal mammal, very closely related to primates and with a highly evolved visual system. It is also an important difference to take into account considering the multitude of studies on the mouse visual system in recent years.

The authors additionally present neuronal activity in mice, from three different visual cortical areas recorded with both electrophysiology and imaging. Their conclusions are mostly supported by the data, but some aspects of the recordings and data analysis need to be clarified and extended.

The main issues are outlined below roughly in order of importance:

1) The most worrying aspect is that, if I interpret their figures correctly, their recordings seem not very stable and this may account for many of the differences across the visual conditions. The authors do not report in which order the different stimuli were shown, their supplemental movie, however, makes it seem as though they were not recorded fully interleaved, but potentially in a block design with all cross1 positions recorded first, before switching to cross2 positions and then on to iso... If I interpret Figure 6a correctly, each line is the same neuron and the gray scale shows the average response rate for each condition. Many of these neurons, however, show a large change in activity between the cross1 and the cross2 block. Much larger than the variability within each block that should be due to figure location and orientation tuning. If this interpretation is correct, this would mean that either there were significant brain state changes (they do have the mice on a ball but don't report whether and how much the animals were moving) between the blocks or their recordings could be unstable in time. It would be good to know whether similar dramatic changes in overall activity level occur between the blocks also in their imaging data.

The same might be true for differences in the maps between conditions in figure 4. If indeed the recordings were in blocks and some cells stopped responding, this could explain the low map similarities. For example Cell 1 for the cross stimuli seems to be a simple ON cell, almost like their idealized cell in 3d. However, even though the exact texture in the RF and large parts of the surround for a large part of the locations is exactly identical for Cross1 and Iso2, as well as Cross2 and Iso1, the cells responses for both iso conditions appear to only be noise, or at least extremely noise dominated. Why would the cell not respond in a phase or luminance dependent manner here?

This could either be due to very high surround suppression in the iso condition (which cannot be judged within condition normalization) or because the cell simply responded much weaker due to recording instability or brain state changes. Without any evidence of significant visual responses, enough spikes in each condition and a stable recording across all blocks, this data is not really interpretable. Instability or generally lower firing rates could easily also explain differences in their decoding accuracy.

Similarly, it is very hard to judge the quality of their imaging data. They show no example field of views or calcium response traces and never directly compare this data to their electrophysiology data. It is mentioned that the imaging data is noisy and qualitatively similar, but some quantification could help convince the reader. Even if noisy, it is puzzling that the decoding accuracy should be so much worse with the imaging data: Even with ten times more included neurons, accuracy still does not even reach 30% of that of the ephys data. This could point to very poor data quality.

We address the issue of stability of selectivity in our response to all reviewers above. Note that we wavered on whether to include the imaging data at all given the much better decoding accuracies from the electrophysiology data, and decided to include it for two main reasons:

1) It qualitatively gives a very similar result, namely that there is a texture-dependent ability to resolve the position of given figures, suggesting that the rodent visual system is indeed better equipped at representing figure locations for the cross and iso stimuli than that nat stimulus.

2) The correspondence on subsequent days between single cells and their corresponding spatial preference responses suggests that this is a stable and consistent preference represented by these neurons.

The following verbiage has been added to the methods section

Matching cells across days. Cells were tracked across days by first re-targeting to the same plane by eye such that the mean fluorescence image on a given day was matched to that on the previous day, with online visual feedback provided by a custom software plugin for Scanbox. […] This result points to the consistency of the spatial responses in the visual cortex as a substrate for inferring figure position.

2) There is no information on the recorded units given. Were they spike sorted? Did they try to distinguish fast spiking and regular spiking units? What layers were they recorded from? It is well known that there are large laminar differences in the strength of figure ground modulation, as well as orientation tuned surround suppression. If most of their data would be from layer 5, perhaps a lack of clear figure modulation might not be that surprising. This could perhaps also be seen when comparing their electrophysiology data to the imaging data which is reportedly from layer 2/3, where most neurons show larger figure modulation/tuned surround suppression effects. There is, however, no report or discussion of differences in modulation between recording modalities.

We used Kilosort (Pachitariu et al., 2016) for spike sorting of the data. The output of the automatic template-matching algorithm from Kilosort was visualized on Phy and then curated manually.

We did not compute current source density. The 64 contacts on our probe spanned 1 mm, so we recorded cells throughout all layers of cortex. We didn’t focus on specific layer, as we didn’t find strong modulation by figure/ground or border ownership in any of our cells. We did not distinguish the fast and regular spike units.

3) There is an apparent discrepancy between Figure 5d and i. How can their modulation index be around -0.1 for cross (Figure 5d) - which would correspond to on average ~20% weaker responses to a figure than to background, when their PSTH (5i) shows an almost 50% increase of figure over ground. This positive figure modulation has also been widely reported in the literature (Schnabel, Kirchberger, Keller). Are there different populations of cells going into these analyses?

There was a mismatch in cells for plotting the F/G modulation index and time-course, since we previously set different criteria. Now we used the same criteria and replotted Figure 5d, e, g, h.

4) In a similar vein, it is not immediately clear why the average map correlation would be bigger for random cell pairs (~0.2, Fig 3g) than for the different conditions of the same cell (~0, Fig 5b). Could this be due to differences in recording modality (imaging in 3g and ephys in 5b)?

We suspect the reviewer is correct, namely, that the difference in recording modality accounts for these differences. The spatial mixing of signals inherent to calcium imaging can be problematic for the study of these figure ground and border ownership signals. Thus, it can be assumed that the non-zero mean observed in Fig 3g, is likely due to neuropil contamination, whereas Fig. 5 is purely ephys data and thus has no such confounds.

5) The maps in Figure 4 should show the location of the RF, because they cannot be interpreted without knowledge of the RF center and size. For example cell 4 in the iso 1 condition could be a border cell, or could respond to the center of the figure. It is impossible to deduce without knowledge of the location of the RF.

We have added the following clarification to the figure legend for Fig. 4a:

“Overlaid on these example stimuli are grids representing the 128 possible figure positions and a green ellipse representing the ON receptive field. Note that this receptive field is the Gaussian fit from the sparse noise experiment.”

We have also added the following clarification to the figure legend for Fig. 4b:

“Please note that for all of these experiments the population receptive field was centered on the grid of positions.”

6) It could help the reader to discuss the interpretation of the map correlations in Fig 5 a and b in more detail. My guess is that negatively correlated maps (within cross or iso condition) could come from highly orientation tuned neurons, whereas higher correlation values point to more generally figure/contextually modulated cells (within this condition). While the distribution is far from bimodal, this does not rule out a population of nicely figured modulated cells at the high end of the distribution. It might not be necessary at the level of V1 that the figure modulation be consistent across all textures. It would not be surprising, if orientation contrast-defined, phase contrast-defined and motion contrast-defined figures could be signalled to higher areas by discrete populations of V1 or even LM cells.

We agree the reviewer’s interpretation of the neural findings is possible. But at least from the behavior, it seems unlikely that a motion contrast-defined figure is generated anywhere in the rodent brain.

7) Some of the behavioural results warrant a little more explanation or discussion, as well. In Figure 2h, the mice seem significantly better on the static version of the iso task, than on the moving one. If statistically significant, this should be discussed. Is this because the static frame was maximally phase offset? Then the figure would indeed be better visible better (bigger phase contrast in more frames) than in the moving condition.

Yes, indeed, in Figure 2h, the static frame was chosen with maximal positional displacement, and thus the figure can likely be seen better. We have added this clarification to the figure legend for Fig. 2h.

Figure 2 and extended Figure 1c: why is the mouse lemur performing so poorly on average? It also appears to have biggest problems with the cross stimulus early on in training.

The behavior experiments in the mouse lemur were carried out under an international collaboration and with substantially less exploratory experiments than was done for mouse, treeshrew, and macaque. For the mouse lemur, we simply went with a training regimen that we knew had worked efficiently for treeshrews and without any optimization of the procedure. Thus we would caution against over-interpreting the exact learning rates of the mouse lemurs and instead focus on the qualitative result that they could generalize for the Nat condition. This was a marked departure from the rodents and shrews and is the main finding we would like to convey. We suspect that with future optimizations of behavior shaping, training times and performances could likely both be improved.

Tree shrews seem not to be able to memorize the textures as well as the mice do. Is this because of less deprivation/motivation? Or because of the bigger set of textures in training? This would make memorization harder and could thus lower their overall performance. The comparative aspects are very interesting but the absolute differences in performance could be discussed in more detail or explained better.

Reviewer 1 raised a similar concern, please see our response above

8) In Figure 7b, why wouldn't the explanation for the linear decodability in cross also hold for iso? There are phase offsets at the borders that simple cells should readily be able to resolve, just as in the case of orientation discontinuities. Could they make a surround phase model, similar to their surround orientation model, that could more readily capture the iso discontinuities?

The reviewer is likely correct in their assertion that one could consider further hand tuning the model to account for the observed diversity in responses (namely, Cross > Iso > Nat for figure position decoding). We went directly to a DNN to model the data, since we thought this would be more powerful, given that the DNN features were not tuned to explain our neural data per se.