This passage is the exact moment that the woman can see her full identity. When she finally makes the connection she has been avoiding. The woman who was behind the pattern was herself, she had been the one stopping and creeping.

Thanks to Re*Define and Kaisernet, the original 2005 English-language translation of io [Christmas Eve], a freeware Japanese visual novel written in KiriKiri, is playable in English. The 2005 patch ceased working due to the Japanese game receiving a minor update in 2006. Kaisernet notes that "[t]he fix has been tested on Windows XP and Windows 10." I personally tested it on Linux running the game with the patch on WINE and found that it works without issue.

Interesting project to make it possible to run some Steam games that ordinarily would require Steam to be running to run without Steam.

These are concrete details about the environment of one "sad night" when I experienced depressive emotions. It is due to the learning in class that concrete details help readers to be in the story and understand the author.

Sports on its own causes an emotional response, i can imagine adding a political dimension on top of that made this situation crazy

What is wrong with these people? I get sports, but man this is scary behavior.

He may not of ment to start the revolution of the ages for the French people, but he def. had the big say and position to put an end to it. He became the voice of the people.

so I have my own opinions of professional athletes and their intragame tantrums but I still feel on top of an uncontrolled temper that Richard suffered from CTE and the more I read this the more it is supported, makes for a terrible situation

Author Response

Reviewer #1 (Public Review):

The authors succeeded in fitting their Jansen-Rit model parameters to accurately reproduce individual TEPs. This is a major success already and the first study of this kind to the best of my knowledge. Then the authors make use of this fitted model to introduce virtual lesions in specific time windows after stimulation to analyze which of the response waveforms are local and which come from recurrent circles inside the network. The methodological steps are nicely explained. The authors use a novel parameter fitting method that proves very successful. They use completely openly available data sets and publish their code in a manner that makes reproduction easy. I really enjoyed reading this paper and suspect its methodology to set a new landmark in the field of brain stimulation simulation. The conclusions of the authors are well supported by their results, however, some analysis steps should be clarified, which are specified in the essential revisions.

We are delighted and flattered by the Reviewer’s positive evaluation of our work, and appreciation of our efforts to maximize its reproducibility. We wish also to thank the Reviewer for their compelling and interesting points, which we have addressed in full, and we believe further enhance the quality of the paper. Thanks again!

Reviewer #2 (Public Review):

Here the authors tackle the problem of identifying which parts of a TMS-evoked response are local to the stimulation site versus driven by reverberant activity from other regions. To do this they use a dataset of EEG recorded simultaneously with TMS pulses, and examine virtual lesions of a network of neural masses fitted to the data. The fitting uses a very recent model inversion method developed by the authors, able to fit time series directly rather than just summary statistics thereof. And it apparently works rather well indeed, at least after the first ~50 ms post-stimulus. I expect many readers will be keen to try this fitting method in their own work.

We are delighted by the Reviewer’s appreciation and consideration of our paper. We have addressed the comments and revisions requested following the flow suggested by the Reviewer’s comments. We would take this opportunity to kindly thank the Reviewer for his/her contribution and for helping us to improve the manuscript.

Reviewer #3 (Public Review):

The manuscript is very well written and the graphics are quite iconic. Moreover, the hypothesis is clear and the rationale is very convincing. Overall, the paper has the potential of being of paramount importance for the TMS-EEG community because it provides a valuable tool for a proper interpretation of several previously published TMS-EEG results.

Unfortunately, in my opinion, the dataset used to train and validate the method does not support the implication and interpretation of the results. Indeed, as clearly visible from most of the figures and mentioned by the authors of the database, the data contains residual sensory artifacts (auditory or somatosensory) that can completely bias the authors' interpretation of the re-entrant activity.

We are most grateful to the Reviewer for their positive evaluation of our manuscript. We also sincerely appreciate all the comments and suggestions raised, and for contributing their evident expertise with TMS-EEG data towards the constructive improvement of this research. We hope the Reviewer will appreciate our efforts made to address their excellent points, and are pleased with the resultant strengthening of the paper.

Reviewer #1 (Public Review):

The authors succeeded in fitting their Jansen-Rit model parameters to accurately reproduce individual TEPs. This is a major success already and the first study of this kind to the best of my knowledge. Then the authors make use of this fitted model to introduce virtual lesions in specific time windows after stimulation to analyze which of the response waveforms are local and which come from recurrent circles inside the network. The methodological steps are nicely explained. The authors use a novel parameter fitting method that proves very successful. They use completely openly available data sets and publish their code in a manner that makes reproduction easy. I really enjoyed reading this paper and suspect its methodology to set a new landmark in the field of brain stimulation simulation. The conclusions of the authors are well supported by their results, however, some analysis steps should be clarified, which are specified in the essential revisions.

This is scary to think about. Those passionate fans had to have been in so much fear too. Sports can bring out the worst in people.

its unfortunate this happens still to this day. How the few can ruin it for the many.

I can't imagine this taking place,

Scary and Crazy out of control.... to witness that would be awful

They were upset because of the game suspensions. Sports have always had that effect on the fan base, they will go act out whether something went their way or not. A good example of this is the Philidelphia Eagles fan base.

Author Response:

We thank the three reviewers for their thoughtful comments and constructive critique.

Reviewer #1 (Public Review):

Hu et al. present findings that extend the understanding of the cellular and synaptic basis of fast network oscillations in the sensory cortex. They developed the ex vivo model system to study synaptic mechanisms of ultrafast (>400Hz) network oscillation ("ripplets") elicited in layer 4 (L4) of the barrel cortex in the mouse brain slice by optogenetically activating thalamocortical axon terminals at L4, which mimic the thalamic transmission of somatosensory information to the cortex. This model allowed them to reproduce extracellular ripplet oscillations in the slice preparation and investigate the temporal relationship of cellular and synaptic response in fast-spiking (FS) inhibitory interneurons and regular spiking (RS) with extracellular ripplet oscillations to common excitatory inputs at these cells. FS cells show precisely timed firing of spike bursts at ripplet frequency, and these spikes are highly synchronized with neighboring FS cells. Moreover, the phase-locked temporal relationship between the ripplets and responses of FS and RS cells, although different phases, to thalamocortical activation are found to closely coincide with EPSCs in RS cells, which suggests that common excitatory inputs to FS and RS cells and their synaptic connectivity are essential to generate reverberating network activity as ripplet oscillations. Additionally, they show that spikes of FS cells in layer 5 (L5) reduced in the slice with a cut between L4 and L5, proposing that recurrent excitation from L4 excitatory cells induced by thalamocortical optogenetic stimulation is necessary to drive FS spike bursts in layer 5 (L5).

Overall, this study helps extend our knowledge of the synaptic mechanisms of ultrafast oscillations in the sensory cortex. However, it would have been nice if the authors had utilized various methodologies and systems.

Although the overall findings are interesting, the conclusion of the study could have been strengthened according to the following points:

1. The authors investigate the temporal relationship between ripplets and FS and RS cells' response elicited by optogenetic activation of TC axon terminals, which is mainly supported by phase-locked responses of FS and RS cells with local ripplets oscillations to optogenetic activation. They also show highly synchronized FS-FS firing by eliminating electrical gap-junction and inhibitory synaptic connections to this synchrony. Based on these findings, the authors suggest that common excitatory inputs to FS and RS cells in L4 would be essential to generate these local ripplets. However, it interferes with the ability to follow the logical flow for biding other findings of phase-locking responses of FS and RS cells in ripplet oscillations in L4.

We understand the reviewer’s issue with the logical flow of our argument. We will address this concern by textual changes and/or by rearranging the order of the presentation and figures.

2. The authors suggest that the optogenetic activation of TC axon terminal elicits local ripplet oscillations via synchronized spike burst of FS inhibitory interneurons and alternating EPSC-IPSC of RS cells in phase-locked with ripplets in L4 barrel cortex, which would be generated by following common excitatory inputs from the local circuits to these cells at the ripple frequency. Thus they intend to investigate the source of these excitatory inputs at this local network of L4 by suppressing the firing of L4 RS cells. However, they show FS spike bursts in L5B, instead of L4, due to the technical limitations of their experimental setup, as described in the manuscript. Although L5 FS spike bursts decrease after cutting the L4/L5 boundary, supposedly inhibiting excitatory input from L4 as depicted in Fig 6D in the author's manuscript, the interpretation of data seems overly extended because it does not necessarily represent cellular and synaptic activities which are phase-locked with the ripplets observed in L4.

We have not studied network oscillation in layer 5 at the same level of detail we have studied layer 4; however the oscillations in both layers are phase locked. We will show this as supplemental data in the revised manuscript.

3. Authors suggested a circuit model. It would be recommended that the authors try to perform in silico analysis using the suggested model to explore the function of thalamocortical axons on the fast-spiking and regular-spiking neurons to support their circuit model.

We agree that a computational model of the layer 4 network, demonstrating ripplets in silico, would enhance our understanding of this re-discovered ultrafast oscillation. Moreover, such a model would also help constrain the allowable parameter space of other, existing models of layer 4 or of the complete cortical column, as the ability of these existing models to recreate ripplets in response to strong, synchronous thalamocortical activation could now be used as a stringent test of the assumptions underlying these models. We hope to reproduce ripplets in silico, within an experimentally constrained parameter space, in a near future study.

Reviewer #2 (Public Review):

This manuscript studied potential cellular mechanisms that generate ultrafast oscillations (250-600Hz) in the cortex. These oscillations correlate with sensory stimulation and might be relevant for the perception of relevant sensory inputs. The authors combined ex-vivo whole-cell patch-clamp recordings, local field potential (LFP) recordings, and optogenetic stimulation of thalamocortical afferents. In a technical tour de force, they recorded pairs of fast-spiking (FS)-FS and FS-regular-spiking (RS) neurons in the cortex and correlated their activity with the LFP signal.

Optogenetic activation of thalamic afferents generated ripple-like extracellular waveforms in the cortex, which the authors referred to as ripplets. The timing of the peaks and troughs within these ripplets was consistent across slices and animals. Activation of thalamic inputs induced precisely timed FS spike bursts and RS spikes, which were phase-locked to the ripplet oscillation. The authors described the sequences of RS and FS neuron discharge and how they phase-locked to the ripplet, providing a model for the cellular mechanism generating the ripplet.

The manuscript is well-written and guides the reader step by step into the detailed analysis of the timing of ripplets and cellular discharges. The authors appropriately cite the known literature about ultrafast oscillations and carefully compare the novel ripplets to the well-known hippocampal ripples. The methods used (ex-vivo patch-clamp and LFP) were appropriate to study the cellular mechanisms underlying the ripplets.

Overall, this manuscript develops means for studying the role of cortical ultrafast oscillations and proposes a coherent model for the cellular mechanism underlying these cortical ultrafast oscillations.

We thank the reviewer for his supportive comments.

Reviewer #3 (Public Review):

In this study, Hu et al. aimed to identify the neuronal basis of ultrafast network oscillations in S1 layer 4 and 5 evoked by the optogenetic activation of thalamocortical afferents in vitro. Although earlier in vivo demonstration of this short-lived (~25 ms) oscillation is sparse and its significance in detecting salient stimuli is not known the available publications clearly show that the phenomenon is consistently present in the sensory systems of several species including humans.

In this study using optogenetic activation of thalamocortical (TC) fibers as a proxy for a strong sensory stimulus the in vitro model accurately captures the in vivo phenomenon. The authors measure the features of oscillatory LFP signals together with the intracellular activity of fast-spiking (FS) interneurons in layer 4 and 5 as well as in layer 4 regular spiking (RS) cells. They accurately measure the coherence of intra- and extracellular activity and convincingly demonstrate the synchronous firing of FS cells and antiphase firing of RS and FS cells relative to the field oscillation.

Major points:

1) The authors conclude the FS cell network has a primary role in setting the frequency of the oscillation. While these data are highly plausible and entirely consistent with the literature only correlational not causal results are shown thus direct demonstration of the critical role of GABAergic mechanisms is missing.

We find that blocking fast inhibition (by puffing a gabazine solution locally) converts ripplets into long-duration paroxysmal events with high-frequency firing of both RS and FS cells. While we do not think that this experiment is diagnostic in distinguishing between competing models (in all models fast inhibition is a necessary component), we will add these experiments as supplemental material.

2) The authors put a strong emphasis on the role of RS-RS interactions in maintaining the oscillation once it was launched by a TC activity. Its direct demonstration, however, is not presented. The alternative scenario is that TC excitation provides a tonic excitatory background drive (or envelope) for interacting FS cells which then impose ultrafast, synchronized IPSPs on RS cells. Similar to the RS-RS drive in this scenario RS cells can also only fire in the "windows of opportunity" which explains their antiphase activity relative to FS cells, but RS cells themselves do not participate in the maintenance of oscillation. Distinguishing between these two scenarios is critical to assess the potential impact of ultrafast oscillation in sensory transmission. If TC inputs are critical the magnitude of thalamic activity will set the threshold for the oscillation if RS-RS interactions are important intracortical operation will build up the activity in a graded manner.

Earlier theoretical studies (e.g Brunel and Wang, 2003; Geisler et al., 2005) strongly suggested that even in the case of the much slower hippocampal ripples (below 200 Hz) phasic activation of local excitatory cells cannot operate at these frequencies. Indeed, rise time, propagation, and integration of EPSPs can likely not take place in the millisecond (or submillisecond) range required for efficient RS-RS interactions. The alternative scenario (tonic excitatory background coupled with FS-FS interactions) on the other hand has been clearly demonstrated in the case of the CA3 ripples in the hippocampus (Schlingloff et al., 2014. J.Nsci).

The Schlingloff et al. study is important, and we actually think that their results, and many of their conclusions, are consistent with our own. We agree with these authors that “…PV cells are essential for the initiation and maintenance of sharp waves and the generation of ripple oscillations”, that “…perisomatic inhibition enforces ripple synchrony by phase-locking firing during SWRs”, and also that “…neuronal coupling via gap junctions is not essential in ripple synchronization”. We also agree that “The tonic excitatory ‘envelope’ arising from the buildup of activity of PCs drives the firing of PV cells”, as far as initiation of ripples in CA3 is concerned. In our model system, thalamocortical excitation serves the same role, of initiating the oscillation. However I do not see how the data of Schlingloff et al. support the conclusion that (in the legend to their Fig. 11) “…there is no cycle-by-cycle reciprocal interaction between the PCs and the PV [interneurons]”, or the implication that FS cells function as independent pacemakers “…because of their reciprocal inhibition”, as their FINO model suggests. The Schlingloff et al. data clearly show cycle-by-cycle alternations of EPSCs and IPSCs (their Fig. 1C, D, as well as their Fig. 7B), as we show in our Fig. 5A. These phasic EPSCs, occurring at ripple frequency, by necessity originate from pyramidal cells synchronized (as a population) to the ripple oscillation, as indeed shown in their multi-unit recordings. This precise, phasic (and clearly not “tonic”) excitatory drive cannot be uncoupled from the ripple (or ripplet) oscillation, and therefore cannot be dismissed as a factor driving the oscillation.

The strongest evidence the Schlingloff et al. study provides that FS cells synchronize independently of excitatory cells – and then impose this oscillation on the excitatory cells - is in their demonstration of ripples generated by prolonged direct optogenetic stimulation of PV cells, in the presence of glutamatergic blockers (their Fig. 6). However this manipulation worked only in some of their slices, and the oscillations only lasted as long as the light stimulus and therefore were exogenously driven rather than network driven. They do not show intracellular responses from either inhibitory or excitatory cells, nor multi-unit activity, during this manipulation, so it is difficult to know if excitatory cells were indeed entrained to the same frequency, as the FINO model posits. Nevertheless this is a very interesting experiment which we plan to attempt in our own model system in a future study.

When the properties of the ultrafast oscillation were tested as various stimulation strengths (Figure 2) weaker stimulation resulted in less precise timing. If TC input is indeed required only to launch the oscillation not to maintain it, this is not expected since once a critical number of RS cells were involved to start the activity their rhythmicity should no longer depend on the magnitude of the initial input. On the other hand, if the entire transient oscillation depends on TC excitation weaker input would result in less precise firing.

Our interpretation for the lesser spike precision with a weaker optogenetic stimulation is that fewer FS cells fired upon the initial thalamocortical volley, and therefore a weaker IPSP wavefront was propagated to RS cells allowing for a wider “window of opportunity” for RS firing,  and this loss of synchrony then propagated from cycle to cycle. This interpretation will be added in the revised manuscript.

3) The experiments indicating the spread of phasic activity from L4 RS to L5 FS cells can not be accepted as fully conclusive. The horizontal cut not only severed the L4 RS to L5 FS connections but also many TC inputs to the L5 FS apical dendrites as well as the axons of L4 FS cells to L5 FS cells both of which can be pivotal in the translaminar spread.

FS cells do not have apical dendrites so we assume the reviewer meant to say “L5 RS apical dendrites”; however if the cut reduced the excitability of L5 RS cells, that only strengthens our conclusion that RS firing is required for maintaining the oscillation. While the cut could have also disrupted L4 FS to L5 FS connections, we are not aware of any evidence that such inter-laminar connections exist. On the other hand, the Pluta et al. 2015 study shows very robust excitatory connections between L4 RS and L5 FS cells.  

Having said that, we agree with the reviewer (indeed, with all three reviewers) that the L4/L5 cut experiments are not conclusive, and we will make this clear in our discussion in the revised manuscript. We plan to do a more conclusive test of our model by using a transgenic line to express inhibitory opsins specifically in L4. This will require expressing ChR2 in the thalamus by virus injection and a careful comparison of ripplets between the two models; we therefore reserve these experiments to a future study.

Reviewer #3 (Public Review):

In this study, Hu et al. aimed to identify the neuronal basis of ultrafast network oscillations in S1 layer 4 and 5 evoked by the optogenetic activation of thalamocortical afferents in vitro. Although earlier in vivo demonstration of this short-lived (~25 ms) oscillation is sparse and its significance in detecting salient stimuli is not known the available publications clearly show that the phenomenon is consistently present in the sensory systems of several species including humans.

In this study using optogenetic activation of thalamocortical (TC) fibers as a proxy for a strong sensory stimulus the in vitro model accurately captures the in vivo phenomenon. The authors measure the features of oscillatory LFP signals together with the intracellular activity of fast-spiking (FS) interneurons in layer 4 and 5 as well as in layer 4 regular spiking (RS) cells. They accurately measure the coherence of intra- and extracellular activity and convincingly demonstrate the synchronous firing of FS cells and antiphase firing of RS and FS cells relative to the field oscillation.

Major points:

1) The authors conclude the FS cell network has a primary role in setting the frequency of the oscillation. While these data are highly plausible and entirely consistent with the literature only correlational not causal results are shown thus direct demonstration of the critical role of GABAergic mechanisms is missing.

2) The authors put a strong emphasis on the role of RS-RS interactions in maintaining the oscillation once it was launched by a TC activity. Its direct demonstration, however, is not presented. The alternative scenario is that TC excitation provides a tonic excitatory background drive (or envelope) for interacting FS cells which then impose ultrafast, synchronized IPSPs on RS cells. Similar to the RS-RS drive in this scenario RS cells can also only fire in the "windows of opportunity" which explains their antiphase activity relative to FS cells, but RS cells themselves do not participate in the maintenance of oscillation. Distinguishing between these two scenarios is critical to assess the potential impact of ultrafast oscillation in sensory transmission. If TC inputs are critical the magnitude of thalamic activity will set the threshold for the oscillation if RS-RS interactions are important intracortical operation will build up the activity in a graded manner.

Earlier theoretical studies (e.g Brunel and Wang, 2003; Geisler et al., 2005) strongly suggested that even in the case of the much slower hippocampal ripples (below 200 Hz) phasic activation of local excitatory cells cannot operate at these frequencies. Indeed, rise time, propagation, and integration of EPSPs can likely not take place in the millisecond (or submillisecond) range required for efficient RS-RS interactions. The alternative scenario (tonic excitatory background coupled with FS-FS interactions) on the other hand has been clearly demonstrated in the case of the CA3 ripples in the hippocampus (Schlingloff et al., 2014. J.Nsci).

When the properties of the ultrafast oscillation were tested as various stimulation strengths (Figure 2) weaker stimulation resulted in less precise timing. If TC input is indeed required only to launch the oscillation not to maintain it, this is not expected since once a critical number of RS cells were involved to start the activity their rhythmicity should no longer depend on the magnitude of the initial input. On the other hand, if the entire transient oscillation depends on TC excitation weaker input would result in less precise firing.

3) The experiments indicating the spread of phasic activity from L4 RS to L5 FS cells can not be accepted as fully conclusive. The horizontal cut not only severed the L4 RS to L5 FS connections but also many TC inputs to the L5 FS apical dendrites as well as the axons of L4 FS cells to L5 FS cells both of which can be pivotal in the translaminar spread.

Because of the way the narrator says that John takes care of her to the point that he, "is very careful and loving, and hardly lets me stir without special direction", I feel like it's fitting that she's in a nursery because she's treated like a child and John's the overbearing mother. By the windows being "barred for little children" it suggests that the narrator is imprisoned.

Author Response

Reviewer #1 (Public Review):

This paper describes the results of a MEG study where participants listened to classical MIDI music. The authors then use lagged linear regression (with 5-fold cross-validation) to predict the response of the MEG signal using (1) note onsets (2) several additional acoustic features (3) a measure of note surprise computed from one of several models. The authors find that the surprise regressors predict additional variance above and beyond that already predicted by the other note onset and acoustic features (the "baseline" model), which serves as a replication of a recent study by Di Liberto.

They compute note surprisal using four models (1) a hand-crafted Bayesian model designed to reflect some of the dominant statistical properties of Western music (Temperley) (2) an ngram model trained on one musical piece (IDyOM stm) (3) an n-gram model trained on a much larger corpus (IDyOM ltm) (4) a transformer DNN trained on a mix of polyphonic and monophonic music (MT). For each model, they train the model using varying amounts of context.

They find that the transformer model (MT) and long-term n-gram model (IDyOM stm) give the best neural prediction accuracy, both of which give ~3% improvement in predicted correlation values relative to their baseline model. In addition, they find that for all models, the prediction scores are maximal for contexts of ~2-7 notes. These neural results do not appear to reflect the overall accuracy of the models tested since the short-term n-gram model outperforms the long-term n-gram model and the music transformer's accuracy improves substantially with additional context beyond 7 notes. The authors replicate all these findings in a separate EEG experiment from the Di Liberto paper.

Overall, this is a clean, nicely-conducted study. However, the conclusions do not follow from the results for two main reasons:

1) Different features of natural stimuli are almost always correlated with each other to some extent, and as a consequence, a feature (e.g., surprise) can predict the neural response even if it doesn't drive that response. The standard approach to dealing with this problem, taken here, is to test if a feature improves the prediction accuracy of a model above and beyond that of a baseline model (using cross-validation to avoid over-fitting). If the feature improves prediction accuracy, then one can conclude that the feature contributes additional, unique variance. However, there are two key problems: (1) the space of possible features to control for is vast, and there will almost always be uncontrolled-for features (2) the relationship between the relevant control features and the neural response could be nonlinear. As a consequence, if some new feature (here surprise) contributes a little bit of additional variance, this could easily reflect additional un-controlled features or some nonlinear relationship that was not captured by the linear model. This problem becomes more acute the smaller the effect size since even a small inaccuracy in the control model could explain the resulting finding. This problem is not specific to this study but is a problem nonetheless.

We understand the reviewer’s point and agree that it indeed applies not exclusively to the present study, but likely to many studies in this field and beyond. We disagree, however, that it constitutes a problem per se. We maintain that the approach of adding a feature, observing that it increases crossvalidated prediction performance, and concluding that therefore the feature is relevant, is a valid one. Indeed, it is possible and even likely that not all relevant features (or non-linear transformations thereof) will be present in the control/baseline model. If a to-be-tested feature increases predictive performance and therefore explains relevant variance, then that means that part of what drives the neural response is non-trivially related to the to-be-tested feature. The true underlying relationship may not be linear, and later work may uncover more complex relationships that subsume the earlier discovery, but the original conclusion remains justified.

Importantly, we wish to emphasize that the key conclusions of our study primarily rest upon comparisons between regression models that are by design equally complex, such as surpriseaccording-to-MT versus surprise-according-to-IDyOM and comparisons across different context lengths. We maintain that the comparison with the Baseline model is also important, but even taking the reviewer’s worry here into account, the comparison between different equally-complex regression models should not suffer from it to the same extent as a model-versus-baseline comparison.

2) The authors make a distinction between "Gestalt-like principles" and "statistical learning" but they never define was is meant by this distinction. The Temperley model encodes a variety of important statistics of Western music, including statistics such as keys that are unlikely to reflect generic Gestalt principles. The Temperley model builds in some additional structure such as the notion of a key, which the n-gram and transformer models must learn from scratch. In general, the models being compared differ in so many ways that it is hard to conclude much about what is driving the observed differences in prediction accuracy, particularly given the small effect sizes. The context manipulation is more controlled, and the fact that neural prediction accuracy dissociates from the model performance is potentially interesting. However, I am not confident that the authors have a good neural index of surprise for the reasons described above, and this limits the conclusions that can be drawn from this manipulation.

First of all, we would like to apologize for any unclarity regarding the distinction between Gestalt-like and statistical models. We take Gestalt-like models to be those that explain music perception as following a restricted set of rules, such as that adjacent notes tend to be close in pitch. In contrast, as the reviewer correctly points out, statistical learning models have no such a priori principles and must learn similar or other principles from scratch. Importantly, the distinction between these two classes of models is not one we make for the first time in the context of music perception. Gestalt-like models have a long tradition in musicology and the study of music cognition dating back to (Meyer, 1957). The Implication-Realization model developed by Eugene Narmour (Narmour, 1990, 1992; Schellenberg, 1997) is another example for a rule-based theory of music listening, which has influenced the model by David Temperley, which we applied as the most recently influential Gestalt-model of melodic expectations in the present study. Concurrently to the development of Gestalt-like models, a second strand of research framed music listening in light of information theory and statistical learning (Bharucha, 1987; Cohen, 1962; Conklin & Witten, 1995; Pearce & Wiggins, 2012). Previous work has made the same distinction and compared models of music along the same axis (Krumhansl, 2015; Morgan et al., 2019a; Temperley, 2014). We have updated the manuscript to elaborate on this distinction and highlight that it is not uncommon.

Second, we emphasize that we compare the models directly in terms of their predictive performance both of upcoming musical notes and of neural responses. This predictive performance is not dependent on the internal details of any particular model; e.g. in principle it would be possible to include a “human expert” model where we ask professional composers to predict upcoming notes given a previous context. Because of this independence of the relevant comparison metric on model details, we believe comparing the models is justified. Again, this is in line with previously published work in music (Morgan et al., 2019a), language, (Heilbron et al., 2022; Schmitt et al., 2021; Wilcox et al., 2020), and other domains (Planton et al., 2021). Such work compares different models in how well they align with human statistical expectations by assessing how well different models explain predictability/surprise effects in behavioral and/or brain responses.

Third, regarding the doubts on the neural index of surprise used: we respond to this concern below, after reviewer 1’s first point to which the present comment refers (the referred-to comment was not included in the “essential revisions” here).

Reviewer #2 (Public Review):

This manuscript focuses on the basis of musical expectations/predictions, both in terms of the basis of the rules by which these are generated, and the neural signatures of surprise elicited by violation of these predictions.

Expectation generation models directly compared were gestalt-like, n-gram, and a recentlydeveloped Music Transformer model. Both shorter and longer temporal windows of sampling were also compared, with striking differences in performance between models.

Surprise (defined as per convention as negative log prior probability of the current note) responses were assessed in the form of evoked response time series, recorded separately with both MEG and EEG (the latter in a previously recorded freely available dataset). M/EEG data correlated best with surprise derived from musical models that emphasised long-term learned experiences over short-term statistical regularities for rule learning. Conversely, the best performance was obtained when models were applied to only the most recent few notes, rather than longer stimulus histories.

Uncertainty was also computed as an independent variable, defined as entropy, and equivalent to the expected surprise of the upcoming note (sum of the probability of each value times surprise associated with that note value). Uncertainty did not improve predictive performance on M/EEG data, so was judged not to have distinct neural correlates in this study.

The paradigm used was listening to naturalistic musical melodies.

A time-resolved multiple regression analysis was used, incorporating a number of binary and continuous variables to capture note onsets, contextual factors, and outlier events, in addition to the statistical regressors of interest derived from the compared models.

Regression data were subjected to non-parametric spatiotemporal cluster analysis, with weights from significant clusters projected into scalp space as planar gradiometers and into source space as two equivalent current dipoles per cluster

General comments:

The research questions are sound, with a clear precedent of similar positive findings, but numerous unanswered questions and unexplored avenues

I think there are at least two good reasons to study this kind of statistical response with music: firstly that it is relevant to the music itself; secondly, because the statistical rules of music are at least partially separable from lower-level processes such as neural adaptation.

Whilst some of the underlying theory and implementation of the musical theory are beyond my expertise, the choice, implementation, fitting, and comparison of statistical models of music seem robust and meticulous.

The MEG and EEG data processing is also in line with accepted best practice and meticulously performed.

The manuscript is very well-written and free from grammatical or other minor errors.

The discussion strikes a brilliant balance of clearly laying out the interim conclusions and advances, whilst being open about caveats and limitations.

Overall, the manuscript presents a range of highly interesting findings which will appeal to a broad audience, based on rigorous experimental work, meticulous analysis, and fair and clear reporting.

We thank the reviewer for their detailed and positive evaluation of our manuscript.

Reviewer #3 (Public Review):

The authors compare the ability of several models of musical predictions in their accuracy and in their ability to explain neural data from MEG and EEG experiments. The results allow both methodological advancements by introducing models that represent advancements over the current state of the art and theoretical advancements to infer the effects of long and shortterm exposure on prediction. The results are clear and the interpretation is for the most part well reasoned.

At the same time, there are important aspects to consider. First, the authors may overstate the advancement of the Music Transformer with the present stimuli, as its increase in performance requires a considerably longer context than the other models. Secondly, the Baseline model, to which the other models are compared, does not contain any pitch information on which these models operate. As such, it's unclear if the advancements of these models come from being based on new information or the operations it performs on this information as claimed. Lastly, the source analysis yields some surprising results that don't fit with previous literature. For example, the authors show that onsets to notes are encoded in Broca's area, whereas it should be expected more likely in the primary auditory cortex. While this issue is not discussed by the authors, it may put the rest of the source analysis into question.

While these issues are serious ones, the work still makes important advancements for the field and I commend the authors on a remarkably clear and straightforward text advancing the modeling of predictions in continuous sequences.

We thank the reviewer for their compliments.

Reviewer #2 (Public Review):

This manuscript focuses on the basis of musical expectations/predictions, both in terms of the basis of the rules by which these are generated, and the neural signatures of surprise elicited by violation of these predictions.

Expectation generation models directly compared were gestalt-like, n-gram, and a recently-developed Music Transformer model. Both shorter and longer temporal windows of sampling were also compared, with striking differences in performance between models.

Surprise (defined as per convention as negative log prior probability of the current note) responses were assessed in the form of evoked response time series, recorded separately with both MEG and EEG (the latter in a previously recorded freely available dataset). M/EEG data correlated best with surprise derived from musical models that emphasised long-term learned experiences over short-term statistical regularities for rule learning. Conversely, the best performance was obtained when models were applied to only the most recent few notes, rather than longer stimulus histories.

Uncertainty was also computed as an independent variable, defined as entropy, and equivalent to the expected surprise of the upcoming note (sum of the probability of each value times surprise associated with that note value). Uncertainty did not improve predictive performance on M/EEG data, so was judged not to have distinct neural correlates in this study.

The paradigm used was listening to naturalistic musical melodies.

A time-resolved multiple regression analysis was used, incorporating a number of binary and continuous variables to capture note onsets, contextual factors, and outlier events, in addition to the statistical regressors of interest derived from the compared models.

Regression data were subjected to non-parametric spatiotemporal cluster analysis, with weights from significant clusters projected into scalp space as planar gradiometers and into source space as two equivalent current dipoles per cluster

General comments:

The research questions are sound, with a clear precedent of similar positive findings, but numerous unanswered questions and unexplored avenues

I think there are at least two good reasons to study this kind of statistical response with music: firstly that it is relevant to the music itself; secondly, because the statistical rules of music are at least partially separable from lower-level processes such as neural adaptation.

Whilst some of the underlying theory and implementation of the musical theory are beyond my expertise, the choice, implementation, fitting, and comparison of statistical models of music seem robust and meticulous.

The MEG and EEG data processing is also in line with accepted best practice and meticulously performed.

The manuscript is very well-written and free from grammatical or other minor errors.

The discussion strikes a brilliant balance of clearly laying out the interim conclusions and advances, whilst being open about caveats and limitations.

Overall, the manuscript presents a range of highly interesting findings which will appeal to a broad audience, based on rigorous experimental work, meticulous analysis, and fair and clear reporting.

It sounds like hope is lost, and the person is singing about trying to enjoy some of the joys in life without the pain while battling this hopelessness.

Could be standing up for what's right and going against the academic school system but in return, they were punished for standing up.

Command for getting hardware type of mouse via Windows PowerShell.

I came here after reading a couple articles (one on Super User & one on MS's help forums) recommending X-Mouse Button Control as a general way to disable back buttons on mice.

Note: this doesn't seem to work on Windows 11 for Microsoft USB IntelliMouse Optical.

History:: private members club

Reaction: A suffragist who believes in peace was trying to make themselves different from a suffragette. They didn't want to be counted as one of them.

I dunno about this assessment...

They knew, and they tried.

They just eventually stopped trying, because they beat Netscape and Sun.

Yeah, but they're basically cribbing the paradigm introduced by the Lisa and popularized by the Mac in 1984. (At least that used to be the case—before Chrome introduced the hamburger menu and everyone else followed suit, Microsoft's attempt to change things up with the ribbon not withstanding.)

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.

Irrational response

Maybe a link to our own opinionated Python binaries would be good to have here ?

Maybe a link to our own opinionated R binaries would be good to have here ?

msys2

The C/C++ extension does not include a C++ compiler or debugger. You will need to install these tools or use those already installed on your computer.

The English blame the French, the French blame the English.

They've always been like this : )

Reviewer #2 (Public Review):

Fuhrman et al. explore a fascinating system to study the evolution and genetic architecture of ecological adaptation in marine midges. They use a number of approaches including analyses of whole genome sequences and QTL mapping to explore population structure and the loci associated with the timing and mode of reproduction. I have some concerns about the analyses and interpretations which I outline below.

1) My primary concern is in the design and interpretation of the QTL analysis. The QTL approach used here has low power, both due to the sample size and the number of markers used (it looks like ~8 per chromosome). The authors use an analysis of the sex determining locus as a "control" but because of the complete heritability of this trait in most systems it is more of a straw man to me. The authors conclude that the architecture of the trait is polygenic based on this, but we are missing key information to evaluate this.

2) There are some issues with the presentation and interpretation of the population genetic analyses. Many assumptions are made about whether introgression or ILS occurred and there are statements that are not accurate about it being "impossible" to distinguish between these scenarios.

3) Some of the analyses associated with ecological adaptation that follow on the QTL results struck me as ad hoc and with the potential to lead to spurious results. I am not familiar with the BayPass approach but since it is the approach that explicitly accounts for population structure it seems the one that would be most appropriate for the authors to focus on in a revised manuscript. The use of phylogenetic windows that associate with ecotype is concerning to me as given the level of ILS and gene flow that appears to be present in this system is would be very challenging to distinguish signal from noise.

4) There were issues with the GO analysis that should be addressed. Because the gene universe used for GO enrichment is a subset of the full gene set, GO enrichment results will be biased. This will mostly lead to false positives (i.e. overrepresentation of a GO category due to evaluating a subset of genes that fall in that category).

load url and run script

protection against too much globalization

There are few of churches that have this same original look, most of these churches are Cathedrals. There are some beauties up in the Cleveland/ Lakewood area.

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.

I came to this page looking for a way to disable news stories in Windows 11 Widgets. I attempted one of the solutions (Disable Interests From Widgets To Turn Off News Feeds) but News recommendations still appeared.

Since I mainly wanted the Widget enabled for a calendar view, I decided against using Widgets altogether and settled for using the calendar in the notifications bar.

Another alternative I considered was to have 4 static Widgets pinned to obscure any news articles in the feed. However, unless one uses the insider Windows 11 build 25211 or later, Widget display will pop up from mouse hovering.

Useful PowerShell command to do recursive file search in Windows through PowerShell.

Someone recommending to avoid using Dell SupportAssist on Windows 11. I came across this because I was trying to see if there was a way to update SA in order to ensure the driver iqvw64e.sys was removed. Related to the problem here. Uninstalling SupportAssist resolved the aforementioned problem since recursive file search through C drive failed to find driver iqvw64e.sys

Based on other comments in this thread, seems like it's best to let Windows Update handle the drivers. Will no longer use Dell SA and will utilize "Optional Updates" to handle drivers

Currently, the only perceived benefit from SA is automating support tickets submissions if product is under warranty. Last IT support experience with Dell was positive (they did the best they could), but they didn't know much about sys admin stuff on Windows (weren't very helpful in resolving issue without losing all files and installed software).

I came here looking for a way to resolve an error "A driver cannot load on this device" for the driver "iqvw64e.sys". This error popped up after I enabled "memory integrity" in Windows 11.

Note that "some malware camouflages itself as iqvw64e.sys" source.

This driver is associated with Intel network connections software, and gets removed by uninstalling the software per this reddit comment in r/sysadmin. This error is probably because Intel won't support Intel PROSet & Intel Advanced Network Services on Windows 11. The driver is likely a holdover from my Windows 10 OS before I upgraded it to Windows 11. The driver is probably unneeded since other Intel drivers are available .

The accepted answer in this Microsoft Q&A forum seems silly (just disable memory integrity), so I kept reading and found the highlighted response which quoted a more sensible answer (get rid of bad drivers). Later in the replies, someone asks what's the most efficient way to remove the driver and someone else states

I found the solution to this problem. After digging for the source of this file, I came across this article. File.net description of iqvw64e.sys. According to the article, this driver can be removed by uninstalling "Intel(R) Network Connections". Sure enough, I went to Control Panel, uninstalled the recommended app, rebooted, and voila! No more error. As for the value of that application, I have no idea. I am however happy to be rid of this error.

This didn't work for my case since "Intel(R) Network Connections" wasn't installed. Couldn't find iqvw64e.sys in the expected location of C:\Windows\System32\drivers. May have been removed after memory integrity enabled?

Presently looks like non-issue and can disregard warning in the future

I came to this page looking for a way to add Xournal++ to the official winget repository. The accepted answer seems like it might do this: https://stackoverflow.com/a/64367435/6457597

Need to open issue on GH repo about creating manifest file for Xournal++

Resources The resources used in this document are technological, since it uses a laboratory experimental design.

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• Repeated facade - entrance to windows for lighting

• 'Present' for the people of Rome from those higher up in the hierarchy
• Similar symmetrical layouts
• Large windows facilitate lighting
• Directionality towards an alter
• Decorated with iconography

The downfall of computing was when they invented, enfored copy right on system created in the open.

As long there is a licence we all loose!

Then you can privatize 20 years of development in the commons called Linux

If you can beat them run it inside a proprietary operating system. Better still, rely on emulators for old windows so you no longer need to worry about backward compatibiity

Info Select was on this list of DEVONthink Windows alternatives. Looks like "personal information management" preceded the boom of "personal knowledge management"

From a discussion on DEVONthink alternatives for Windows users.

Reference for UltraRecall (UR) being the most DEVONthink like Windows alternative. No mobile companion for UR. Look into this being paired with Obsidian

Trouble shooting git add . issue.

Setting method one for Windows system working with others:

git config --global core.autocrlf true

Someone giving a troubleshooting solution to using Joe Glines' Auto Hotkey script that inserts text from a list of the user's choosing. The problem another user had was including it in their main script file, but this was resolved with Louis Burki's answer

Solution to AutoHotkey text replacement bug. Just add sleep parameter. Adding {Sleep 250} should generally work

A brief tutorial on PowerToys Run that has some handy tricks listed

Winstall is a way to bulk install WIndows apps quickly with Windows Package Manager (winget)

Oh NOOOOOOO; although I would be remiss to mention the fact that this was a common treatment (for up until actually very recently and even now it is considered by some to be beneficial) to get some fresh air so opening the windows when it was stuffy was thought to rid the place of sickness, which there's an extent at which this is true, though it is rooted in the idea of miasma and miasma was basically the idea that sickness traveled through the air by way of smells and stuffiness and things like that--and again it's not completely wrong but it's also not germ theory.

https://www.loc.gov/resource/cph.3c19546/ Fifth Ave., New York City, with two buses on street.

= gloss - a knife capable if cutting windows between worlds

Description of Hyndland

.

Windows 10, Microsoft teams, etc.

Pro of coupling to Wayland: can use expressive free WM animation! Con: Nobody will ever be able to try your system on Windows or MacOS

281022 193603 6-301 R15. SL<br /> o Point for READ

Crime has a significant effect on the entire New York City community, but especially on the low income community. Many NYC officials prioritize minimizing the effect of the law on criminals over minimizing the effect of criminals on law-abiding citizens.

Tod

Author Response

Reviewer #1 (Public Review):

This paper introduces a new statistical framework to study cellular lineages and traits. Several new measures are introduced to infer selection strength from individual lineages. The key observation is that one can simply relate cumulants of a fitness landscape to population growth, and all of this can be simply computed from one generating function, that can be inferred from data. This formalism is then applied to experimental cell lineage data.

I think this is a very interesting and clever paper. However, in its current form the paper is very hard to read, with very few explanations beyond the mathematical observations/definitions, which makes it almost unreadable for people outside of the field in my opinion. Some more intuitive explanations should be given for a broader audience, on all aspects : definitions of fitness « landscape », selection strength(s), connections between cumulants and other properties (including skewness) etc... There are many new definitions given with names reminiscent of classical concepts in evolutionary theory, but the connection is not always obvious. It would be great to better explain with very simple, intuitive examples, what they mean, beyond maths, possibly with simple examples. Some of this might be obvious to population geneticists, and in fact some explanations made in discussion are more illuminating, but earlier would be much better. I give more specific comments below.

We thank the reviewer for calling our attention to the lack of accessible explanations on the significant terms and quantities in this framework. Following the suggestion in the comments below, we added Box 1, providing intuitive and plain explanations on the terms of fitness, fitness landscape, selection, selection strength, and cumulants. In each section, we explain the standard usage of these terms in evolutionary biology and clarify the similarities and differences in this framework. We also added a figure to Box 1 and provided a schematic explanation of the relationships among chronological and retrospective distributions, fitness landscapes, and selection strength. We believe that these explanations and a figure would better clarify the meanings and functions of these quantities.

Major comments :

1) the authors give names to several functions, for instance before equation (1) they mention « fitness landscape », then describe « net fitness » , which allows the authors to define « fitness cumulants ». Later on, a « selection » is defined. Those terms might mean different things for different authors depending on the context, to the point there are sometimes almost confusing. For instance, why is h a « landscape » ? For me, a landscape is kind of like a potential, and I really do not see how this is connected to h. « fitness cumulants » is particularly jargonic. There are also two kinds of selection strengths, which is very confusing. I would recommend that the authors make a glossary of the term, explain intuitively what they mean and maybe connect them to standard definitions.

We appreciate the suggestion of making a glossary of the terms. Following the suggestion, we added Box 1 to provide intuitive and plain explanations of the terms used in this framework.

In Box 1, we explain why we called h(x) a fitness landscape, referring to its standard usage in evolutionary biology. In evolutionary biology, fitness landscapes (also called adaptive landscapes) are visual representations of relationships between reproductive abilities (fitness) and genotypes. The height of landscapes corresponds to fitness. Since constructing "genotype space" is usually difficult, fitness is often mapped on an allele frequency or phenotype (trait) space to depict a "landscape." Fitness landscapes introduced in our framework are analogous to those in evolutionary biology in that fitness differences are mapped on trait spaces. Although fitness landscapes in evolutionary biology are usually metaphorical or conceptual tools for understanding evolutionary processes, the landscapes in our framework are directly measurable from division count and trait dynamics on cellular lineages.

We also explain "selection" and "selection strength" in Box 1. As pointed out, we define three kinds of selection strength measures. These three measures share a similar property of reporting the overall correlations between traits and fitness. However, they also have critical differences regarding additional selection effects they represent: S_KL^((1)) for growth rate gain, S_KL^((2)) for additional loss of growth rate under perturbations, and their difference S_KL^((2))-S_KL^((1)) for the effect of selection on fitness variance. We restructured the sections in Results and clarified these important meanings of the different selection strength measures.

We removed the term "fitness cumulants" as this is non-general and might cause confusion to readers. We now rephrased this more precisely as "cumulants of a fitness landscape (with respect to chronological distribution)." Besides, we added a general explanation of "cumulants" to Box 1 and clarified what first, second, and third-order cumulants represent about distributions.

2) Along the same line, it would be good to give more intuitive explanations of the different functions introduced. For instance I find (2) more intuitive than (1) to define h . I think some more intuition on what the authors call selection strengths would be super useful . In Table 1 selection strengths are related to Kublack Leibler divergence (which does not seem to be defined), it would be good to better explain this.

In addition to Box 1, we included more intuitive explanations on fitness landscapes and selection strength where they first appear in the Theoretical background section. As pointed out, descriptions of the linkage between the selection strength measures and Kullback-Leibler divergence were only in the Supplemental Information in the original manuscript. We now explicitly show this linkage where we first define the selection strength.

Following this comment, we also changed the definition of a fitness landscape from the original one to h(x)≔τΛ+ln⁡〖Q_rs (x)/Q_cl (x)〗 (Eq. 1), using the chronological and retrospective distributions introduced in the preceding paragraph. This definition is mathematically equivalent to the previous one, but we believe it is more intuitive.

3) It seems to me the authors implicitly assume that, along a lineage, one would have almost stationary phenotypes (e.g. constant division rate) . However, one could imagine very different situations, for instance the division rates could depend on interactions with other cells in the growing population, and thus change with time along a lineage. One could also have some strong random components of division rate over time . I am wondering how those more complex cases would impact the results and the discussion

We thank the reviewer for pointing out our insufficient explanation of an essential feature of this framework. As we now explain in the "Examples of biological questions" section (L62-65) and Discussion (L492-493), this framework does not assume stationary phenotypes (traits) on cellular lineages. On the contrary, we developed this framework so that one can quantify fitness and selection strength even for non-stationary phenotypes (traits) due to factors such as non-constant environments and inherent stochasticity.

In fact, if traits are stationary in cellular lineages, this framework becomes essentially identical to the individual-based evolutionary biology framework (see ref. 26, for example). Our framework assumes a cell lineage as a unit of selection and any measurable quantities along cellular lineages as lineage traits, whether they are stationary or non-stationary. Therefore, our framework can evaluate fitness landscapes and selection strength without explicitly taking the environmental conditions around cells into account. This means that h(x) and S[X] in this framework extract the correlations between the traits of interest and division counts among various factors that could potentially influence division counts. On the other hand, this framework has a limitation due to this design: it cannot say anything about the influence of factors such as non-quantified traits and potential variations in environmental conditions. We now explain these important points explicitly in the revised manuscript (L493-496).

Likewise, stochasticity in division rate does affect division count distributions, and its influence appears as differences in the selection strength of division count S[D]. As stated in the text, S[D] sets the maximum bound for the selection strength of any lineage trait (L143-145). Therefore, S_rel [X]≔S[X]/S[D] reports the relative strength of the correlation between the trait X and lineage fitness in a given level of S[D] in each condition.

To clarify the influence of stochasticity in division rate, we present a cell population model in which cells divide stochastically according to generation time (interdivision time) distributions in Appendix 2 (we moved this section from the Supplemental Information with modifications). We can confirm from this model that the shapes of generation time distributions influence the selection strength S[D]. Importantly, one can understand from this model that stochasticity in generation times constantly introduces selection to cell populations and modulates the growth rate and selection strength even in the long-term limit. We now clarify this important point in the Discussion (L519-526).

4) « Therefore, in contrast to a common assumption that selection necessarily decreases fitness variance, here we show that under certain conditions selection can increase fitness variance among cellular ». This is a super interesting statement, but there is such a lack of explanations and intuition here that it is obscure to me what actually happens here.

When a decrease in fitness variance by selection is mentioned in evolutionary biology, an upper bound and inheritance of fitness across the generations of individuals are usually assumed. In such circumstances, selection drives the fitness distribution toward the maximum value, and the selection eventually causes fitness variance to decrease. However, even in this process, a decrease is not assured for every step; whether selection reduces fitness variance at each step depends on the fitness distribution at that time.

In our argument, we compared fitness variances between chronological and retrospective distributions. We showed both theoretically and experimentally that there are cases where the variances of the retrospective distributions (distributions after selection) become larger than those of the chronological distributions (distributions before selection). The direction of variance change depends on the shape of chronological distributions, primarily on the skewness of the distributions (positive skew for increasing the variance and negative skew for decreasing the variance). The direction of variance changes can also be probed by the difference between the two selection strength measures S_KL^((2))-S_KL^((1)). Notably, we can demonstrate that there are cases where retrospective fitness variances are larger than chronological fitness variances even in the long-term limit, as shown by a cell population model in Appendix 2.

We now explain what kind of situations are usually premised when reduction of fitness variance is mentioned and clarify that, in our framework, we compare the fitness variances between chronological and retrospective distributions (L542-548). We also explain that a selection effect on fitness variance generally depends on fitness distribution and that a larger fitness variance in retrospective distribution is possible even in the long-term limit (L548-557).

Reviewer #2 (Public Review):

The paper addresses a fundamental question: how do phenotypic variations among lineages relate to the growth rate of a population. A mathematical framework is presented which focuses on lineage traits, i.e. the value of a quantitative trait averaged over a cell lineage, thus defining a fitness landscape h(x). Several measures of selection strengths are introduced, whose relationships are clarified through the introduction of the cumulant generating function of h(x). These relationships are illustrated in analytical mathematical models and examined in the context of experimental data. It is found that higher than third order cumulants are negligible when cells are in early exponential phase but not when they are regrowing from a stationary phase.

The framework is elegant and its independence from mechanistic models appealing. The statistical approach is broadly applicable to lineage data, which are becoming increasingly available, and can for instance be used to identify the conditions under which specific traits are subject to selection.

We appreciate the reviewer for the positive evaluation. We will reply to your specific comments below.

Reviewer #3 (Public Review):

In this work the authors have constructed a useful mathematical framework to delineate contributions leading to differences in lineages of populations of cells. In principle, the framework is widely applicable to exponentially growing populations. An attractive feature is that the framework is not tailored to particular growth models or environmental conditions. I expect it will be valuable for systems where contributions from phenotypic heterogeneity overwhelm contributions from intrinsic stochasticity in cellular dynamics.

I am generally very positive about this work. Nevertheless, a few specific concerns:

1) In here, lineages are considered as fitter if they have more division events. But this consideration neglects inherent stochasticity in division events. Even in a completely homogeneous population, the number of division events for different lineages is different due to intrinsic stochasticity, but applying the methods discussed in this manuscript may lead to falsely assigning different fitness levels to different lineages. The reason why (despite having different number of division events) these lineages ought be assigned the same fitness level is that future generations of these cells will have identical statistics, in contrast with those of cells that are phenotypically different. Extending the idea to heterogeneous populations, the actual difference in fitness levels may be significantly different from what is obtained from the mathematical framework presented here, depending on the level of inherent stochasticity.

We thank the reviewer for the comment on the point of which our explanation was insufficient in the original manuscript. Intrinsic stochasticity in interdivision time (generation time) is, in fact, critical for selection. For example, if a cell divides with a generation time shorter than the average due to stochasticity, this cell is likely to have more descendant cells in the future population on average than the other cells born at the same timing, even if the descendants follow identical statistics. Therefore, the properties of intrinsic stochasticity, including shapes of generation time distributions and transgenerational correlations, significantly affect the overall selection strength S_KL^((1)) [D] (and also S_KL^((2)) [D]). We now explain this important point in the Results section, referring to the analytical model in Appendix 2 (L327-334), and also in Discussion (L519-524).

Importantly, even when cell division processes seem purely stochastic, different states in some traits might underlie these variations in generation times. In such cases, evaluating h(x) and S_rel [X] can still unravel the correlations between the trait values and fitness. Especially, the relative selection strength S_rel [X]≔S_KL^((1) ) [X]/S_KL^((1) ) [D] extracts the correlation of the trait values in a given level of division count heterogeneity in each condition. We now clarify this important aspect of the framework in Discussion (L524-526).

When a cell population is composed of heterogeneous subpopulations each of which follows a distinct statistical rule, our framework evaluates the combined effects from the heterogeneous rules and the inherent stochasticity of each subpopulation. Untangling these two contributions is generally challenging unless we have appropriate markers for distinguishing the subpopulations. However, when the subpopulations follow significantly distinct statistics, the division count distribution should become skewed or multimodal, and the difference between the two selection strength measures S_KL^((2) ) [D]-S_KL^((1) ) [D] can suggest the existence of such subpopulations. Therefore, detailed analyses using all the selection strength measures and the fitness landscapes can provide insights into cell populations’ internal structures and selection.

We now explain the effect of inherent stochasticity in generation times (L327-334 and L519-524) and discuss how we can probe the existence of subpopulations based on the selection strength measures (L508-512). Please also refer to our reply to the comment 3 of reviewer #1.

2) In one of the sections the authors mention having performed analytical calculations for a cellular population in which cells divide with gamma distributed uncorrelated interdivision times. It's unclear if 1) within specific sub-populations, cells with the sub-population divide with the same division time, and the distribution of division times is due to the diverse distribution of sub-populations; or 2) if there are no such sub-populations and all cells stochastically choose division time from the same distribution irrespective of their past lineage. If the latter, then I do not see the need for a lineage-based mathematical formulation when the problem can dealt with in much simpler traditional ways which so not keep track of lineages.

We dealt with the situation of 2) in this model. As noted by the reviewer, we can calculate the chronological and retrospective mean fitness and the population growth rate by a simpler individual-based age-structured population model (see ref. 10, for example). However, applying this framework to this model can clarify the utility of the cumulant generating function, the meaning of the differences between these fitness measures, and the effect of statistical properties of intrinsic stochasticity on long-term growth rate and selection. Therefore, we kept this model in Appendix 2 (the section is moved from Supplemental Information) with additional clarification of our motivation for analysis and the implication of the results.

3) The analytical calculations provided seem to be exact only for trajectories of almost infinite duration (or in practice, duration much greater than typical interdivision time). For example, if the observation time is of the order of division time, this would create significant artifacts / artificial bias in the weights of lineages depending on whether the cell was able to divide within the observation time or not. Thus, the results claiming that contributions of higher order cumulants become significant in the regrowth from a late stationary phase are questionable, especially since authors note that 90% of cells showed no divisions within the observation time.

We thank the reviewer for an insightful comment. It is true that the duration of observation influences the results. In the regrowing experiments with E. coli, we aimed to compare the two cell populations regrowing from different stages of the stationary phase. Therefore, it is appropriate to fix the time windows between the two conditions. Even though a significant fraction of cell lineages remains undivided, the regrowing cells already divide several times within this time window. Therefore, the results are valid if we compare and discuss the selection levels in this time scale. However, clarification of the selection in the longer time scales requires a more detailed characterization of lag time distributions under both conditions.

We now clarify the range of validity of the results and the limitations on prediction for the long-term selection without knowing the details of the lag time distributions in Discussion (L536-539).

Moment of zombie-ness: The questioning of something if they are between life and death. Eyes are often noted as the windows to the soul and they give off a lot of different emotions. "Dead" eyes, eyes that "light up", "kind" eyes, etc.

Esta solução parece funcionar para resolver o problema da atualização do Gerenciador de Arquivos.

Not prosecuting crimes is a positive trend, apparently. This disregards how NYC transformed itself in the 90s and 00s under the leadership of Mayors Giuliani and Bloomberg, and how that success was maintained at least when former Mayor de Blasio wisely chose William Bratton as NYPD Commissioner.

"Window of opportunity" is a popular concept in political science used to describe how policymakers promote their policies at specific times

Broken windows policing is the "notorious" theory which drove New York City's revival under former Mayor Giuliani in the 1990s.

todo

在窗户材料选择上，欧洲使用玻璃而中国使用纸。

Talvez seja o que estou esperando a anos, integração das pesquisas em todos os produtos da Microsoft.

• windows 64

Social media sites such as Facebook is terrible for this. Put a comment someone does not like and before you know it your windows are put threw.

discussion of steps taken for data analysis

Author Response

Reviewer #1 (Public Review):

Figures 2 through 6. There is no description of the relationship between the findings and the anatomical location of the electrodes (other than distal versus local). Perhaps the non-uniform distribution of electrodes makes these analyses more complicated and such questions might have minimal if any statistical power. But how should we think about the claims in Figures 2-6 in relationship to the hippocampus, amygdala, entorhinal cortex, and parahippocampal gyrus? As one example question out of many, is Figure 2C revealing results for local pairs in all medial temporal lobe areas or any one area in particular? I won't spell out every single anatomical question. But essentially every figure is associated with an anatomical question that is not described in the results.

To address the reviewer’s point we now report the distribution of spike-LFP pairs across anatomical regions for each Figure 2-6. The results split by anatomical regions are reported in Figure 2 – figure supplement 7, Figure 3 – figure supplement 7, Figure 4 – figure supplement 1, Figure 5 – figure supplement 2, and Figure 6 – figure supplement 3. We also calculated a non-parametric Kruskal-Wallis Test to statistically examine the effect of anatomical regions on the results shown in each figure. Generally, these new results show that the effects are similar across regions, apart from two exceptions (i.e. Figure 4 – supplement 1; and Figure 5 – supplement 2). However, we would like to stress that these results should be taken with a huge grain of salt because the electrodes were not evenly distributed across regions (i.e. ~75% of observations pertain to the hippocampus), and patients as the reviewer correctly points out. This leads to sometimes very low numbers of observations per region and it is difficult to disentangle whether any apparent differences are driven by regional differences, or differences between patients. Detailed results are reported below.

Manuscript lines 207-212: “In the above analysis all MTL regions were pooled together to allow for sufficient statistical power. Results separated by anatomical region are reported in Figure 2 – figure supplement 7 for the interested reader. However, these results should be interpreted with caution because electrodes were not evenly distributed across regions and patients making it difficult to disentangle whether any apparent differences are driven by actual anatomical differences, or idiosyncratic differences between patients.”

Manuscript lines 255-258: “Finally, we report the distal spike-LFP results separated by anatomical region in Figure 3 – figure supplement 7, which did not reveal any apparent differences in the memory related modulation of theta spike-LFP coupling between regions.”

Manuscript lines 264-266: “PSI results separated by anatomical regions are reported in Figure 4 – figure supplement 1, which revealed that the PSI results were mostly driven by within regional coupling.”

Manuscript lines 399-303: “We also analyzed whether the memory-dependent effects of cross-frequency coupling differ between anatomical regions (see Figure 5 – figure supplement 2). This analysis revealed that the results were mostly driven by the hippocampus, however we urge caution in interpreting this effect due to the large sampling imbalance across regions.”

Manuscript lines 343-346: “As for the above analysis we also investigated any apparent differences in co-firing between anatomical regions. These results are reported in Figure 6 – figure supplement 3 and show that the earlier co-firing for hits compared to misses was approximately equivalent across regions.”

Figure 1

1A. I assume that image positions are randomized during a cued recall?

Yes, that was the case. We now added that information in the methods section.

Manuscript lines 526: “Image positions on the screen were randomized for each trial.”

What was the correlation between subjects' indication of how many images they thought they remembered and their actual performance?

We did not log how many images the patients thought they remembered. Specifically, if the patients answered that they remembered at least one image, then they were shown the selection screen where they could select the appropriate images. Therefore, we cannot perform this analysis. We report this now in the methods section. However, albeit interesting, the results of such an analysis would not affect the main conclusions of our manuscript.

Manuscript lines 523-524: “The experimental script did not log how many images the patient indicated that they thought to remember.”

1B. Chance is shown for hits but not misses. I assume that hits are defined as both images correct and misses as either 0 or 1 image correct. Then a chance for misses is 1-chance for hits = 5/6. It would be nice to mark this in the figure.

Done as suggested (see Figure 1).

The authors report that both incorrect was 11.9%. By chance, both incorrect should be the same as both correct, hence also 1/6 probability, hence the probability of both incorrect seems quite close to chance levels, right?

Yes, that is correct, however, across sessions the proportion of full misses (i.e. both incorrect) was significantly below chance (t(39)=-1.9214; p<0.05). Nevertheless, the proportion of fully forgotten trials appears to be higher than expected purely by chance. This is likely driven by a tendency of participants to either fully remember an episode, or completely forget it, as demonstrated previously in behavioural work (Joensen et al., 2020; JEP Gen.). We report this now in the manuscript.

Manuscript lines 132-136: “Across sessions the proportion of full misses (i.e. both incorrect) was significantly below chance (t39=-1.92; p<0.05). However, the proportion of fully forgotten trials appears to be higher than expected purely by chance. This is likely driven by a tendency of participants to either fully remember an episode, or completely forget it, as demonstrated previously in behavioral work (25).”

1C. How does the number of electrodes relate to the number of units recorded in each area?

The distribution of neurons per region is shown in the new Figure 1D (see above). It approximately matches the distribution of electrodes per region, except for the Amygdala where slightly more neurons where recorded. This is because of one patient (P08) who had two electrodes in the left and right Amygdala and who contributed at lot of sessions (i.e. 9 sessions, comparing to an average of 4.44 per patient).

Line 152. The authors state that neural firing during encoding was not modulated by memory for the time window of interest. This is slightly surprising given that other studies have shown a correlation between firing rates and memory performance (see Zheng et al Nature Neuroscience 2022 for a recent example). The task here is different from those in other studies, but is there any speculation as to potential differences? What makes firing rates during encoding correlate with subsequent memory in one task and not in another? And why is the interval from 2-3 seconds more interesting than the intervals after 3 seconds where the authors do report changes in firing rates associated with subsequent performance? Is there any reason to think that the interval from 2-3 seconds is where memories are encoded as opposed to the interval after 3 seconds?

Zheng et al. used a movie-based memory paradigm where they manipulated transitions between scenes to identify event cells and boundary cells. They show that boundary cells, which made up 7.24% of all recorded MTL cells, but not event cells (6.2% of all MTL cells) modulate their firing rate around an event depending on later memory. There are quite a few differences between Zheng et al’s study and our study that need to be considered. Most importantly, we did not perform a complex movie-based memory paradigm as in Zheng et al. and therefore cannot identify boundary cells, which would be expected to show the memory dependent firing rate modulation. This alone could contribute to the fact that no significant differences in firing rates in the first second following stimulus onset were observed. Such an absence of a difference of neural firing depending on later memory is not unprecedented. In their seminal paper, Rutishauser et al. (2010; Nature) report no significant differences in firing rates (0-1 seconds after stimulus onset, which is similar to our 2-3 seconds time window) between later remembered or later forgotten images. This finding is also in line to Jutras & Buffalo (2009; J Neurosci) who also show no significant difference in firing rates of hippocampal neurons during encoding of remembered and forgotten images.

The 2-3 seconds time interval, which corresponds to 0-1 seconds after the onset of the two associate images, is special because it marks the earliest time point where memory formation can start, therefore allowing us to investigate these very early neural processes that set the stage for later memory-forming processes. While speculative, these early processes likely capture the initial sweep of information transfer into the MTL memory system which arguably is reflected in the timing of spikes relative to LFPs. It is conceivable that these initial network dynamics reflect attentional processes, which act as a gate keeper to the hippocampus (Moscovitch, 2008; Can J Exp Psychol) and thereby set the stage for later memory forming processes. This interpretation would be consistent with studies in macaques showing that attention increases spike-LFP coupling, whilst not affecting firing rates (Fries et al., 2004; Science). We modified the discussion section to address this issue.

Manuscript lines 468-474: “Interestingly, these early modulations of neural synchronization by memory encoding were observed in the absence of modulations of firing rates, which is consistent with previous results in humans (16) and macaques (12), but contrasts with (43). Studies in macaques showed that attention increases spike-LFP coupling whilst not affecting firing rates (44). It is therefore conceivable that these initial network dynamics reflect attentional processes, which act as a gate keeper to the hippocampus and thereby set the stage for later memory forming processes (45).”

Lines 154-157 and relationship to the subsequent analyses. These lines mention in passing differences in power in low-frequency bands and high-frequency bands. To what extent are subsequent results (especially Figures 3 and 4) related to this observation? That is, are the changes in spike-field coherence, correlated with, or perhaps even dictated by, the changes in power in the corresponding frequency bands?

To address this question we repeated the analysis that we performed for SFC for Power in those channels whose LFP was locally coupled to spikes in gamma, and distally coupled to spikes in theta. Furthermore, we correlated the difference in peak frequency between hits and misses between Power and SFC. If power would dictate the effects seen in SFC then we would expect similar effects of memory in power as in SFC, that is an increase of peak frequency for hits compared to misses for gamma and theta. Furthermore, we would expect to find a correlation between the peak frequency differences in power and SFC. None of these scenarios were confirmed by the data. These results are now reported in Figure 2 – figure supplement 5 for gamma, and Figure 3 – figure supplement 5 for theta.

Manuscript lines 195-199: “We also tested whether a similar shift in peak gamma frequency as observed for spike-LFP coupling is present in LFP power, and whether memory-related differences in peak gamma spike-LFP are correlated with differences in peak gamma power (Figure 2 – figure supplement 5). Both analyses showed no effects, suggesting that the effects in spike-LFP coupling were not coupled to, or driven by similar changes in LFP power.”

Manuscript lines 248-253: “As for gamma, we also tested whether a similar shift in peak theta frequency is present in LFP power, and whether there is a correlation between the memory-related differences in peak theta spike-LFP and peak theta power (Figure 3 – figure supplement 5). Both analyses showed no effects, suggesting that the effects in spike-LFP coupling were not coupled to, or driven by similar changes in LFP power.”

Do local interactions include spike-field coherence measurements from the same microwire (i.e., spikes and LFPs from the same microwire)?

Yes, they do. Out of the 53 local spike-SFC couplings found for the gamma frequency range, 11 (20.75%) were from pairs where the spikes and LFPs were measured on the same microwire. We assume that the reviewer is asking this question because of a concern that spike interpolation may introduce artifacts which may influence the spectrograms and consequently the spike-LFP coupling measures. This was also pointed out by Reviewer #2. To address this concern, we split the data based on whether the spike and LFP providing channels were the same or different. The results show that (i) the spectrogram of SFC is highly similar between the two datasets, with a prominent gamma peak present in both and no significant differences between the two; (ii) restricting the analysis to those data where the LFP and spike providing channels are different replicated the main finding of faster gamma peak frequencies for hits compared to misses; and (iii) limiting the SFC analysis further to only ‘silent’ channels, i.e. channels where no SUA/MUA activity was present at all also replicated the main finding of faster gamma peak frequencies for hits compared to misses.

These analyses suggest that the SFC results were not driven by spike interpolation artefacts.

Manuscript lines 199-203: “To rule out concerns about possible artifacts introduced by spike interpolation we repeated the above analysis for spike-LFP pairs where the spike and LFP providing channels are the same or different, and for ‘silent’ LFP channels (i.e. channels were no SUA/MUA activity was detected (see Figure 2 – figure supplement 6). “

60 Hz. It has always troubled me deeply when results peak at 60 Hz. This is seen in multiple places in the manuscript; e.g., Figures 2B, 2E. What are the odds that engineers choosing the frequency for AC currents would choose the exact same frequency that evolution dictated for interactions of brain signals? This is certainly not the only study that reports interesting observations peaking at 60 Hz. One strong line of argument to suggest that this is not line noise is the difference between conditions. For example, in Figure 2B, there is a difference between local and distal interactions. It is hard for me to imagine why line noise would reveal any such difference. Still ...

The frequency for AC currents in Europe is 50 Hz, not 60 Hz as in the US. Therefore, our SFC effects are well outside the range of the notch.

Figure 6. I was very excited about Figure 6, which is one of the most novel aspects of this study. In addition to the anatomical questions about this figure noted above, I would like to know more. What is the width of the Gaussian envelope?

The width of the Gaussian Window used in the original results was 25ms. We chose this time window because in our view it represents a good balance between integrating over a long-enough time window and thus allowing for some jitter in neural firing between pairs of neurons, whilst still being temporally specific. Finding the right balance here is not trivial because a too short time window underestimates co-firing, and a too long time window may not provide the temporal specificity necessary to detect co-firing lags (Cohen & Kohn, 2011; Nat Neurosci). To test whether this choice critically affected our results, we repeated the analysis for different window sizes, i.e. 15, 35, and 45 ms. The results show that the pattern of results did not change, with hits showing earlier peaks in co-firing compared to misses. Critically, the difference in co-firing peaks was significant for all window sizes, except for the shortest one which presumably is due to the increase in noise because of the smaller time window over which spikes are integrated. These issues are now mentioned in the methods section, and the results for the different window sizes are reported in Figure 6 – figure supplement 4.

Manuscript lines 346-347: “The co-firing analyses were replicated with different smoothing parameters (see Figure 6 – figure supplement 4).”

Manuscript lines 894-898: “We chose this time window because it should represent a good balance between integrating over a long-enough time window and thus allowing for some jitter in neural firing between pairs of neurons, whilst still being temporally specific (57). To test whether this choice critically affected our results, we repeated the analysis for different window sizes, i.e. 15, 35, and 45 ms (see Figure 6 – figure supplement 4).”

Are these units on the same or different microwires?

All units used for the analysis shown in Figure 6 come from different microwires. This was naturally the case because the putative up-stream neuron was distally coupled to the theta LFP, and the putative down-stream neuron was locally coupled to gamma at this same theta LFP electrode. This information is listed in Figure 6 – source data 1 which lists the locations and electrode IDs for all neuron pairs shown in figure 6.

How do the spike latencies reported here depend on the firing rates of the two units?

To address this question we first tested whether firing rates (averaged across the putative up-stream and down-stream neurons) differ between hits and misses. If they do, this would be suggestive of a dependency of the spike latency differences between hits and misses on firing rates. No such difference was observed (p>0.3). Second, we correlated the differences between hits and misses in Co-firing peak latencies with the differences in firing rates. Again, no significant correlation was observed (R=-0.06; p>0.7), suggesting that firing rates had no influence on the observed differences in co-firing latencies. These control analyses are now reported in the main text.

Manuscript lines 347-350: “No significant differences in firing rates between hits and misses were found (p>0.3), and on correlations between firing rates and the co-firing latencies were obtained (R=-0.06; p>0.7), suggesting that firing rates had no influence on the observed co-firing differences between hits and misses.”

What do these results look like for other pairs that are not putative upstream/downstream pairs?

As we reported in the original manuscript in lines 352-355 we did not find a memory dependent effect on co-firing latencies if we select neuron pairs solely on the basis of distal theta SFC. Within this analysis the distally theta coupled neuron would be the up-stream neuron and the neuron recorded at the site where the theta LFP is coupled would be the down-stream neuron. This null-result suggests that in order for the memory dependent difference in co-firing lags to emerge, the down-stream neurons need to be coupled to a local gamma rhythm in order for the memory effect on co-firing latencies to emerge. However, within this previous analysis there is still a notion of up-stream and down-stream neurons because neuron pairs were selected based on distal theta phase coupling. We therefore repeated this analysis for all pairs of neurons in a completely unconstrained fashion such that all possible pairs of neurons that were recorded from different electrodes were entered into the co-firing analysis. This analysis also revealed no difference in co-firing lags, neither for positive lags nor for negative lags. Instead, what this analysis showed is tendency for hits to show a higher occurrence of simultaneous or near simultaneous firing, which is in line with Hebbian learning. These results are now reported in Figure 6 – figure supplement 1.

Manuscript lines 333-335: “In addition, a completely unconstrained co-firing analysis where all pairs possible pairings of units were considered also showed no systematic difference in co-firing lags between hits and misses (Figure 6 – figure supplement 1).”

Reviewer #2 (Public Review):

Roux et al. investigated the temporal relationship between spike field coherence (SFC) of locally and distally coupled units in the hippocampus of epilepsy patients to successful and unsuccessful memory encoding and retrieval. They show that SFC to faster theta and gamma oscillations accompany hits (successful memory encoding and retrieval) and that the timing of the SFC between local and distal units for hits comports well with synaptic plasticity rules. The task and data analyses appear to be rigorously done.

Strengths: The manuscript extends previous work in the human medial temporal lobe which has shown that greater SFC accompanies improved memory strength. The cross-regional analyses are interesting and necessary to invoke plasticity mechanisms. They deploy a number of contemporary analyses to disentangle the question they are addressing. Furthermore, their analyses address limitations or confound that can arise from various sources like sample size, firing rates, and signal processing issues.

Weaknesses:

Methodological:

The SFC coherence measures are dependent in part on extracting LFPs derived from the same or potentially other electrodes that are contaminated by spikes, as well as multiunit activity. In the methods, they cite a spike removal approach. Firstly, the incomplete removal or substitution of a signal with a signal that has a semblance to what might have been there if no spike was present can introduce broadband signal time-locked to the spike and create spurious SFC. Can the authors confirm that such an artifact is not present in their analyses? Secondly, how did they deal with the removal of the multiunit activity? It would be suspected that the removal of such activity in light of refractory period violation might be more difficult than well-isolated units, and introduce artifacts and broadband power, again which would spuriously elevate SFC. Conversely, the lack of removal of multiunit activity would seem to for a surety introduce significant broadband power. One way around this might be that since it is uncommon to have units on all 8 of the BF microwires, to exclude the microwire(s) with the units when extracting the LFP to avoid the need to perform spike removal.

The reviewer raises a valid concern which we address as follows. Firstly, an artefact introduced into SFC by linear interpolation would be a problem for those local SFCs where the spike providing channel and the LFP providing channel are identical. Out of the 53 local spike-SFC couplings found for the gamma frequency range, only 11 (20.75%) were from pairs where the spikes and LFPs come from the identical microwire. It is unlikely that this minority of data would have driven the results. Furthermore, it is unlikely that the interpolation would introduce a frequency shift of SFC that is memory dependent, because the interpolation is more likely to cause a general increase in broadband SFC (as opposed to having a frequency band specific effect). However, to address this concern, we split the data based on whether the spike and LFP providing channels were the same or different. The results show that (i) the spectrogram of SFC is highly similar between the two datasets, with a prominent gamma peak present in both and no significant differences between the two; (ii) restricting the analysis to those data where the LFP and spike providing channels are different replicated the main finding of faster gamma peak frequencies for hits compared to misses.

Secondly, we followed the reviewer’s suggestion and repeated the SFC analysis for ‘silent’ microwires, i.e. microwires where no single or multi-units were detected. This analysis replicated the same memory effects as observed in the analysis with all microwires. Specifically, we found an increase in the local gamma peak SFC frequency for hits compared to misses, as well as an increase in distal theta peak SFC frequency for hits compared to misses. These results are reported in the main manuscript and in Figure 2 – figure supplement 6 for gamma, and figure 3 – figure supplement 6 for theta.

Manuscript lines 199-203: “To rule out concerns about possible artifacts introduced by spike interpolation we repeated the above analysis for spike-LFP pairs where the spike and LFP providing channels are the same or different, and for ‘silent’ LFP channels (i.e. channels were no SUA/MUA activity was detected (see Figure 2 – figure supplement 6).”

Manuscript lines 253-255: “We also repeated the above analysis for spike-LFP pairs by only using ‘silent’ LFP channels (i.e. channels were no SUA/MUA activity was detected (see Figure 3 – figure supplement 6) to address possible concerns about artefacts introduced by spike interpolation.”

In a number of analyses the spike train is convolved with a Gaussian in places with a window length of 250ms and in others 25ms. It is suspected that windows of varying lengths would induce "oscillations" of different frequencies, and would thus generate results biased towards the window length used. Can the authors justify their choices where these values are used, and/or provide some sensitivity analyses to show that the results are somewhat independent of the window length of the Gaussian used to convolve with the times series.

The different choices in window length for the Gaussian convolution reflect the different needs of the two analyses where these convolutions were applied. In one analysis we wanted to get a smooth estimate of spike densities that we can average across trials, similar to a peri-stimulus spike histogram. For this analysis we used a window length of 250 ms which we found appropriate to yield a good balance between retaining smooth time courses whilst still being temporally sensitive. Importantly, for the statistical analysis of the firing rates, spike densities were averaged in much larger time windows than 250 ms (i.e. 1 – 2 seconds) therefore our choice of window length for spike densities would not have any bearing on the averaged firing rate analysis.

In the other analysis, which is more central for our manuscript, we used a cross-correlation between spike trains to estimate co-firing lags in the range of milliseconds. Therefore, this analysis necessitated a much higher temporal precision. We used a Gaussian Window with a width of 25ms because it represents a good balance between integrating over a long-enough time window and thus allowing for some jitter in neural firing between pairs of neurons, whilst still being temporally specific. Finding the right balance here is not trivial because a too short time window would be prone to noise and underestimates co-firing, whereas a too long time window may not provide the temporal specificity necessary to detect co-firing lags (Cohen and Kohn, 2013; Nat Neurosci). To test whether this choice critically affected our results, we repeated the analysis for different window sizes, i.e. 15, 35, and 45 ms. The results show that the basic pattern of results did not change, with hits showing earlier peaks in co-firing compared to misses. Critically, the difference in co-firing peaks was significant for all window sizes, except for the shortest one which is likely due to the increase in noise because of the smaller time window over which spikes are integrated. These issues are now mentioned in the methods section, and the results for the different window sizes are reported in Figure 6 – figure supplement 4.

Manuscript lines 346-347: “The co-firing analyses were replicated with different smoothing parameters (see Figure 6 – figure supplement 4).”

Manuscript lines 894-898: “We chose this time window because it should represent a good balance between integrating over a long-enough time window and thus allowing for some jitter in neural firing between pairs of neurons, whilst still being temporally specific (57). To test whether this choice critically affected our results, we repeated the analysis for different window sizes, i.e. 15, 35, and 45 ms (see Figure 6 – figure supplement 4).”

Conceptual:

The co-firing analyses are very interesting and novel. In table S1 are listed locally and distally coupled neurons. There are some pairs for example where the distally coupled neuron is in EC and the downstream one in the hippo, and then there is a pair that is the opposite of this (dist: hippo, local EC). There appear to be a number of such "reversal", despite the delay between these two regions one would assume them to be similar in sign and magnitude given the units are in the same two regions. It seems surprising that in two identical regions of the hippo the flow of information or "causality", could be reversed, when/if one assumes information flows through the system from EC to hippo. This seems unusual and hard to reconcile given what is known about how information flows through the MTL system.

The reviewer is correct that the spike co-firing analysis suggests a bi-directional flow of information between the hippocampus and surrounding MTL regions (e.g. entorhinal cortex; see Figure 6 – figure supplement 3). However, this bi-directional flow of information is not incompatible with neuroanatomy and the memory literature. The entorhinal cortex serves as an interface between the hippocampus and the neocortex with superficial layers providing input into the hippocampus (via the perforant pathway), and the deeper layers receiving output from the hippocampus (van Strien et al., 2009; Nat Rev Neurosci). Therefore, on a purely anatomical basis we can expect to see a bi-directional flow of information between the hippocampus and the entorhinal cortex, albeit in different layers. Importantly, reversals as shown in our Figure 6 – source data 1 involved different microwires and therefore different neurons (i.e. the entorhinal unit in row 1 was recorded from microwire 3, whereas the entorhinal unit in row 2 was recorded from microwire 8). It is conceivable that these two neurons correspond to different layers of the entorhinal cortex and therefore reflect input vs. output paths. Moreover, studies in humans demonstrated that successful encoding of memories depends not only on the input from the entorhinal cortex into the hippocampus, but also on the output of the hippocampal system into the entorhinal cortex, and indeed on the dynamic recurrent interaction between these input and output paths (Maass et al. 2014; Nat Comms; Koster et al., 2018; Neuron). Our bi-directional couplings between hippocampal and surrounding MTL regions (such as the EC) are in line with these findings. We have added a discussion of this issue in the discussion section.

Manuscript lines 447-452: “Notably, the neural co-firing analysis indicates a bidirectional flow of information between the hippocampus and surrounding MTL areas, such as the entorhinal cortex (see Figure 6 – figure supplement 3; Figure 6 – source data 1). This result parallels other studies in humans showing that successful encoding of memories depends not only on the input from surrounding MTL areas into the hippocampus, but also on the output of the hippocampal system into those areas, and indeed on the dynamic recurrent interaction between these input and output paths (43, 44).”

test test

Visual representation allow for people to feel closer because they could see physical appearance?

I chose this quote, as well as the following few sentences, because words and their meanings are all relative. Many words do, in fact, have multiple meanings which vary depending on context. Their meaning is not so fixed as to claim that it exists beyond the realm of language, but rather, the system of language is in place to assign meanings to words.

climax

Author Response

Reviewer #1 (Public Review):

Dotov et al. took joint drumming as a model of human collective dynamics. They tested interpersonal synchronization across progressively larger groups composed of 1, 2, 4 and 8 individuals. They conducted several analyses, generally showing that the stability of group coordination increases with group numerosity. They also propose a model that nicely mirrors some of the results.

The manuscript is very clear and very well written. The introduction covers a lot of relevant literature, including animal models that are very relevant in this field but often ignored by human studies. The methods cover a wide range of distinct analyses, including modelling, giving a comprehensive overview of the data. There are a few small technical differences across the experiments conducted with small vs. large groups, but I think this is to some extent unavoidable (yet, future studies might attempt to improve this). Furthermore, the currently adopted model accounts well for behaviors where all individuals produce a similar output and therefore are "equally important". However, it might be interesting to test to what extent this can be generalized to situations where each individual produces a distinct sound (as in a small orchestra) and therefore might selectively adapt to (more clearly) distinguishable individuals.

We agree that this is important. We discuss this in a new section (4.1) at the end of the discussion. We suggest that heterogeneity makes it possible for other modes of organization to compete with the attractive tendency towards the global average. We also point out that factors such as individual skill, task difficulty, delays, and selective attention enable such heterogeneity in the ensemble.

Similarly, it would be interesting to test to what extent the current results (and model) can be generalized to interactions that more strongly rely on predictive behavior (as there is not much to predict here given that all participants have to drum at a stable, non-changing tempo).

We can only speculate that the present results are less relevant to interactions that rely strongly on predicitive behavior, as behaviour in our simple task could be modeled well by our hybrid single oscillator Kuromoto model. We inserted the idea that the presence of a group rhythm can diminish the demands for individuals to predict each other’s notes, the end of paragraph 1, page 27.

An important implication of this study is that some well-known behaviors typically studied in dyadic interaction might be less prominent when group numerosity increases. I am specifically referring to "speeding up" (also termed "joint rushing") and "tap-by-tap error correction" (Wolf et al., 2019 and Konvalinka et al., 2010, also cited in the manuscript, are two recent examples). I am not sure whether this depends on how the data is analyzed (e.g. averaging the behavior of multiple drummers), yet this might be an important take-home message.

Thank you for the suggestion. We edited to emphasize that the relevant part of the analysis of the drumming data was performed at the individual level and using the same methods as typically done in dyadic tapping (first sentences of Section 2.7.2). Speeding up was the only variable where we used group-averages. For consistency, and to avoid confusion, in the present version we re-did the stats (the changed statistical parameters are highlighted) and figures using the individual data points and we did not observe major changes.

I am confident that this study will have a significant impact on the field, bringing more researchers close to the study of large groups, and generally bridging the gap between human and animal studies of collective behavior.

Reviewer #2 (Public Review):

In this manuscript Dotov et al. study how individuals in a group adjust their rhythms and maintain synchrony while drumming. The authors recognize correctly that most investigation of rhythm interaction examines pairs (dyads) rather than larger groups despite the ubiquity of group situations and interactions in human as well as non-human animals. Their study is both empirical, using human drummers, and modeling, evaluating how well variations of the Kuramoto coupled-oscillator describe timing of grouped drummers. Based on temporal analyses of drumming in groups of different sizes, it is concluded that this coupled oscillator model provides a 'good fit' to the data and that each individual in a group responds to the collective stimulus generated by all neighbors, the 'mean field'.

I have concerns about 1) the overall analysis and testing in the study and about 2) specific aspects of the model and how it relates to human cognition. Because the study is largely empirical, it would be most critical for the authors to propose two - or more - alternative hypotheses for achieving and maintaining synchrony in a group. Ideally, these alternatives would have different predictions, which could be tested by appropriate analyses of drummer timing. For example, in non-human animals, where the problem of rhythm interaction in groups has been examined more thoroughly than in humans, many acoustic species organize their timing by attending largely to a few nearby neighbors and ignoring the rest. Such 'selective attention' is known to occur in species where dyads (and triads) keep time with a Kuramoto oscillator, but the overall timing of the group does not arise from individual responses to the mean field. Can this alternative be evaluated in the drumming data ? Would this alternative fit the drumming data as well as, or better than , the mean field, 'wisdom of the crowd' model ?

These are very important points. The present paper is restricted to a simple task where participants are instructed to synchronize with each other. However, we now more explicitly acknowledge the limitations of our study and include a new section, “Beyond the group average” at the end of the Discussion that is dedicated to this issue and discussed other organizing tendencies that are particularly relevant in larger and more diverse ensembles. In the context of the present task, the relative difference between local and global interactions was likely negligible because of the small differences in timing, from 4 to 16 ms, between the closest and most distant pairs.

It will be interesting in future studies to introduce acoustic heterogeneity by varying the timbre of the instruments, for example. In the present study, the instruments had the same timbre with narrowly varying fundamental frequencies (117-129 Hz in the duets/quartets and 249-284 Hz in the octets), a situation that encourages integration of all the acoustic information. We do point out that the present approach needs to be expanded to be able to account for competitive pressure and selective attention.

The well-known Vicsek model (discussed briefly in paragraph 2, page 15), related to the Kuramoto under certain assumptions, can account for a variety of dynamic behaviors in flocking animals. The ability for selective attention in the form of a heterogeneous coupling matrix, combined with the existence of competitive pressure in the form of negative coupling terms can result in spontaneous formation of clusters and spatiotemporal patterns of movement. This is consistent with prior research in chorusing animals (insects and anurans). Large musical ensembles also involve groupings of instruments such as separate sections that change their relative loudness across time. Typically these are not spontaneous but composed and conducted, yet they may satisfy the same constraints.

We also pointed out that we see these as complementary organizing principles. Even in the Vicsek model, there is a notion of a ‘local order parameter’ whereby individuals are coupled to a group average within a narrow interaction radius. The relative importance of other organization tendencies depends on the layout of the acoustic environment and the competitive and collaborative aspects of the task. Hence, parameters such as delay and individual heterogeneity could act as symmetry breaking terms that enable different stabilities from the basic global group synchrony.

A second concern arises from relying on a hybrid, continuous - pulsed version of the Kuramoto coupled oscillator. If the human drummers in the test could only hear but not see their neighbors, this hybrid model would seem appropriate: Each drummer only receives sensory input at the exact moment when a neighbor's drumstick strikes the drum. But the drummers see as well as hear their neighbors, and they may be receiving a considerable amount of information on their neighbors' rhythms throughout the drum cycle. Can this potential problem be addressed? In general, more attention should be paid to the cognitive aspects of the experiment: What exactly do the individual drummers perceive, and how might they perceive the 'mean field' ?

This is all very relevant. We instructed participants to focus on X’s in the centers of their drums and not look at their peers (edited to mention that in at the end of Section 2.4, page 9). Additionally, the pattern of results for tempo change, cross-correlations, and variability in the dyadic condition was consistent with previous studies that involved purely auditory tapping tasks (emphasized in the begging of paragraph 2, page 26). The best way to address this limitation would be to repeat the study and block the visual contact among participants, as well as include a condition emphasizing visual contact.

It is beyond the scope of the present paper to make model-based predictions of effects of coupling and information availability, but this should be done in future work. For the present paper, we now include a simulation involving continuous coupling (end of section 2.9.2, page 16) and Supplementary Figure 8A) which fails to reproduce the results for variability, results that are well captured by the hybrid continuous-pulsed model we developed, see the Supplementary Materials.

Reviewer #3 (Public Review):

The contribution provides approaches to understanding group behaviour using drumming as a case of collective dynamics. The experimental design is interestingly complemented with the novel application of several methods established in different disciplines. The key strengths of the contribution seem to be concentrated in 1) the combination of theoretical and methodological elements brought from the application of methods from neurosciences and psychology and 2) the methodological diversity and creative debate brought to the study of musical performance, including here the object of study, which looks at group drumming as a cultural trait in many societies.

Even though the experimental design and object of study do not represent an original approach, the proposed procedures and the analytical approaches shed light on elements poorly addressed in music studies. The performers' relationships, feedbacks, differences between solo and ensemble performance and interpersonal organization convey novel ideas to the field and most probably new insights to the methodological part.

It must be mentioned that the authors accepted the challenge of leaving the nauseatic no-frills dyadic tests and tapping experiments in the direction of more culturally comprehensive (and complex) setups. This represents a very important strength of the paper and greatly improves the communication with performers and music studies, which have been affected by the poor impact of predictable non-musical experimental tasks (that can easily generate statistical significant measurements). More specifically, the originality of the experiment-analysis approach provided a novel framework to observe how the axis from individual to collective unfolds in interaction patterns. In special, the emergence of mutual prediction in large groups is quite interesting, although similar results might be found elsewhere.

Thank you for these comments.

On another side, important issues regarding the literature review, experimental design and assumptions should be addressed.

I miss an important part of the literature that reports similar experiments under the thematic framework of musical expressivity/expression, groove, microtiming and timing studies. From the participatory discrepancies proposed in 1980's Keil (1987) to the work of Benadon et al (2018), Guy Madison, colleagues and others, this literature presents formidable studies that could help understand how timing and interactions are structured and conceptualized in the music studies and by musicians and experts. (I declare that I have no recent collaborations with the authors I mentioned throughout the text and that I don't feel comfortable suggesting my own contributions to the field). This is important because there are important ontological concerns in applying methods from sciences to cultural performances.

Thank you for the suggestions. We included a brief discussion in the newly added “Beyond the group average” section at the end of the Discussion, specifically the first paragraph, pages 27-8. We think that expressive timing naturally fits in continuation with the other reviewers’ concerns about how much the idea of the group average generalizes to real musical situations. By design and instruction, we stripped individual expression from the present task. Specific cultural contexts and performance styles may want to escape or at least expressively tackle this constraint of our task, and we believe that now that we have established the mean field as one factor affecting group behaviour, further studies can take on the challenge of developing models that make predictions in more complex situations closer to real musical interactions – and testing those models empirically.

One ontological issue that different cultural phenomena differ from, for example, animal behaviour. For example, the authors consider timing and synchrony in a way that does not comply with cultural concepts: p.4 "Here we consider a musical task in which timing consistency and synchrony is crucial". A large part of the literature mentioned above and evidence found in ethnographic literature indicate that the ability to modulate timing and synchrony-asynchrony elements are part of explicit cultural processes of meaning formation (see, for example, Lucas, Glaura and Clayton, Martin and Leante, Laura (2011) 'Inter-group entrainment in Afro-Brazilian Congado ritual.', Empirical musicology review., 6 (2). pp. 75-102.). Without these idiosyncrasies, what you listen to can't be considered a musical task in context and lacks basic expressivity elements that represent musical meaning on different levels (see, for example, the Swanwick's work about layers/levels of musical discourse formation).

Indeed, this is an important issue. We often use cultural phenomena merely as a motivation but do not dive in the relevant details. Here, in addition to the previous discussion, we now reiterate that the tendency towards the group average is one organizing tendency but there are additional ones, enabled by individual heterogeneity and context. For example, marching bands and chanting crowds probably impose different constraints than individual artistic expression by skillful musicians.

Such plain ideas about the ontology of musical activities (e.g. that musical practice is oriented by precision or synchrony) generate superficial constructs such as precision priority, dance synchrony, imaginary internal oscillators, strict predictive motor planning that are not present in cultural reports, excepting some cultures of classical European music based on notation and shaped by industrial models. The lack of proper cultural framing of the drumming task might also have induced the authors to instruct the participants to minimize "temporal variability" (musical timing) and maintain the rate of the stimulus (musical tempo), even though these limiting tasks mostly take part of musical training in some societies (examples of social drumming in non-western societies barely represent isochronous tempo or timing in any linguistic or conceptual way). The authors should examine how this instruction impacts the validity of results that describe the variability since it was affected by imposed conditions and might have limited the observed behaviour. The reporting of the results in the graphs must also allow the diagnosis of the effect of timing in such small time frame windows of action.

We agree totally. We made changes and tried to be more specific about the cultural framing, delineating contexts where the present ideas are more relevant and where they are less relevant, or at least incomplete (the bottom of page 3, and pages 27-8).

This paragraph has a very poetic sort of flow to it. The author has us move through one of these long drives smoothly. The short fragmented segments referencing different sweets at the diner interrupt that flow with short staccato beats before returning to the norm after.

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Reply to the reviewers

In this section we list all the comments done by the three referees and our corresponding action.

Regarding Reviewer #1:

1. On "mechanical control": The authors show changes in circadian power fraction with changes in YAP and with cytoskeletal inhibitors, but there are no properly-controlled experiments that directly perturb mechanics. The authors show a correlation between YAP nuclear/cytoplasmic ratio and circadian power, but YAP N/C alone is not a readout of mechanotrasndcution, per se. The authors have shown two different experiments where cells are cultured on a stiff (30kPa) substrate and soft substrate (300Pa), but they do not shown a direct comparison of YAP nuclear localization and circadian power under these two conditions in the same experiment. Direct, controlled perturbation of mechanical cues is necessary to support the title's use of the phrase "mechanical control."

We agree with the referee that further mechanical perturbations could strengthen our conclusions. In our original manuscript we directly controlled the mechanical environment by culturing cells on substrates of 300Pa and 30kPa in stiffness. These differences in stiffness were not sufficient to drive changes in circadian power fraction and YAP localisation, as depicted in Fig. 3C (we note that the direct comparison requested by the referee is shown in that figure). We hypothesise that this negative result is due to a very low “rigidity threshold” or to secretion of extracellular matrix that stiffens the initially soft substrate. In any case, we plan to strengthen the “mechanical control” message of our paper with one or more of the below experiments:

A) We will measure circadian power fraction and YAP localisation in even extremer stiffness/adhesion conditions, using 300 Pa and 30 kPa polyacrylamide gels with a different fibronectin coating protocol, as described in Elósegui-Artola et al., 2017. This allows a much finer control of the concentration of fibronectin coated, so we can reach low enough levels to compromise the cell adhesion to the substrate and cross down the threshold that would lead to cytosolic localisation of YAP. We will perform this experiment in presence of the FUD peptide, which inhibits matrix deposition (Tomasini-Johansson et al., 2001; this peptide has already been tested in our lab).

B) We will use the approach described in Fig. 2E to compare the circadian power fraction in cells spread in stadium-shaped islands of 2400 um2 and 1200 um2. Oakes et al., 2014 already showed that traction forces exerted by 3T3 fibroblasts depend on the size of the spread area of the cells, so we expect differences in mechanotransduction that should affect YAP localisation and, if our hypothesis is correct, the RevVNP circadian oscillations.

C) We will abolish the physical connection between the actin cytoskeleton and the nucleus by disrupting the LINC complex via the overexpression of a dominant negative (DN) nesprin-1 KASH domain (Lombardi et al., 2011). The plasmid designed for the inducible overexpression of the DN KASH domain, originally tested in NIH3T3 cells (Mayer et al., 2019), is available in our lab and has been used to prove that uncoupling cytoskeleton and nucleus leads to nuclear YAP decrease in single cells (Kechagia at al., 2022). We will aim to increase the circadian power fraction in low density cells upon the overexpression of the DN KASH domain.

Elosegui-Artola A, Andreu I, Beedle AEM, Lezamiz A, Uroz M, Kosmalska AJ, Oria R, Kechagia JZ, Rico-Lastres P, Le Roux AL, et al (2017) Force Triggers YAP Nuclear Entry by Regulating Transport across Nuclear Pores. Cell 171: 1397-1410.e14

Kechagia Z, Sáez P, Gómez-González M, Zamarbide M, Andreu I, Koorman T, Beedle AEM, Derksen PWB, Trepat X, Arroyo M, et al (2022) The laminin-keratin link shields the nucleus from mechanical deformation and signalling Cell Biology

Lombardi ML, Jaalouk DE, Shanahan CM, Burke B, Roux KJ & Lammerding J (2011) The Interaction between Nesprins and Sun Proteins at the Nuclear Envelope Is Critical for Force Transmission between the Nucleus and Cytoskeleton*. Journal of Biological Chemistry 286: 26743–26753

Mayer CR, Arsenovic PT, Bathula K, Denis KB & Conway DE (2019) Characterization of 3D Printed Stretching Devices for Imaging Force Transmission in Live-Cells. Cel Mol Bioeng 12: 289–300

Oakes PW, Banerjee S, Marchetti MC & Gardel ML (2014) Geometry regulates traction stresses in adherent cells. Biophysical Journal 107: 825–833

Tomasini-Johansson BR, Kaufman NR, Ensenberger MG, Ozeri V, Hanski E & Mosher DF (2001) A 49-Residue Peptide from Adhesin F1 of Streptococcus pyogenes Inhibits Fibronectin Matrix Assembly*. Journal of Biological Chemistry 276: 23430–23439

2. On "via YAP/TAZ": In addition to above, it is necessary to show that the changes in Circadian power fraction induced by mechanical cues in fact require YAP/TAZ signaling. Thus, an experiment comparing soft (300Pa) substrate with Stiff (30kPa) substrate in the presence or absence of YAP/TAZ is necessary to state that YAP and TAZ are the mechanistic mediators of mechanical cues on the clock.

We are currently generating via CRISPR-KO and shRNA silencing a YAP1/TAZ double mutant. We plan to use this cell line in those conditions where YAP is prominently nuclear (low density in stiff substrates) with the purpose of rescuing the RevVNP circadian power fraction.

1. While the TEAD-binding domain mutant experiment is elegant, to claim that TEAD is the transcriptional mediator, it must be demonstrated that this mutant indeed fails to induce TEAD-mediated transcription. This could be simply executed by demonstrating that the CCD mutant expresses reduced CTGF and Cyr61 (for example), compared to the 5SA, under these conditions. Further, endogenous YAP is still active and available to bind to TEAD in this system, which should be discussed.

We plan to carry out quantitative real-time PCR of CTGF and Cyr61 in all the YAP mutants and the control. Regarding the presence of endogenous YAP, we will clarify in the text that a) the overexpression of the different YAP mutants was done in high-density conditions, where endogenous YAP is significantly less localised in the nucleus, and that b) the levels of the exogenous YAP are much higher (we already have western blots showing this).

1. In Figure 3a: The cell perimeter needs to be shown either by actin staining or by brightfield images. The manually marking of cell boundaries is insufficient, specifically because the drugs used in this experiment affect the cytoskeleton. It would be very helpful to see this via actin staining or in the least with brightfield images.

The cell perimeter was drawn based on the cytosolic YAP immunostaining, whose levels are high enough to infer the cell shape (higher resolution images can be attached if necessary). As stated in the manuscript, the YAP nuclear-to-cytosolic ratio is calculated using two adjacent areas of identical size, one inside the nucleus and the other one just outside (see Materials and Methods/Immunostainings), so the exact cell shape is irrelevant for this particular quantification.

Regarding Reviewer #2:

Effects on the circadian clock

1. The authors use the fluorescent reporter created by Nagoshi from sections of the Rev-erbα gene. This reporter is widely used to estimate relative circadian timing in individual cells but it does not provide direct information on the circadian clock activity. In other words, while Reverb rhythmic expression is driven by the clock, it is not known whether less-rhythmic or non-rhythmic expression or change in expression level of Rev-erbα is affecting the core clock. For example, it has been shown that Rev-erbα knock-down cells are rhythmic as long as Rev-erb-beta is present. Thus, one major shortcoming of the current version of the manuscript is the missing dissection between Rev-erbα rhythmicity/expression and the circadian clock. More concretely, it remains unclear whether the change in Rev-erbα expression is a direct effect or caused by a defect clock. Since the authors presume a direct effect of YAP/TAP on Rev-erb expression, the former is likely. If that is the case, the data could be interpreted as that (missing) mechanic stimuli can lead to nuclear YAP/TAZ, which rises the level of Rev-erbα (and maybe interfere with its rhythmic accumulation). Beyond Rev-erbα expression, there may or may not be an effect on the circadian clock (core clock, CCGs). With the current version we do not know since the authors do not look beyond Rev-erbα expression. Thus, the claims on circadian clock or circadian rhythms in their cells is not studied in this version of the manuscript. The current version is still very interesting and provides insights into the Rev-erbα modulation, but additional work would be needed to show links with the core clock machinery. For this the authors could show influence (or at least correlation) of the YAP/TAZ/REVERBA phenotype on the oscillations of core clock genes or clock-controlled genes. Either through the use of alternative (ideally constitutive) reporters (e.g. PER2, BMAL1, fluorescent or LUC), or/and by analyzing RNA/Protein of core clock genes or output genes. This would not be necessary for all experiments, but at least for some were its possible (e.g. experiments with drugs perturbations). Otherwise, any claim like "YAP/TAZ perturbs the circadian clock ..." or "the circadian clock deregulation in nuclear YAP-enriched cells" is potentially flawed and has to be removed/reformulated.

We agree with the reviewer. In order to understand if the core clock is affected, beyond REV-ERBA, by YAP/TAZ expression and localisation, we plan to perform the two experimental approaches explained below. For both of them we will use high-density cells with and without YAP-5SA overexpression since the other conditions (drugs, micropatterned cells, low density) may not render enough cells for analytical approaches that are not based on fluorescent microscopy (real-time qPCR or luminescence recordings). Also, the potential results obtained with YAP-5SA overexpression will be more informative regarding causality YAP-circadian clock than those using the other conditions described in the manuscript.

1. We will use NIH3T3 bmal1::luc cells (already generated in our lab with the pABpuro-BluF plasmid; https://www.addgene.org/46824/) and an adapted microscopy-based system to track bioluminescence. We will need to give our cells a synchronisation shock since the single-cell signal with this reporter is too low and noisy to perform single-cell tracking.
2. We will check during 48 hours, every 4 hours, the mRNA levels of Bmal1, Clock, Cry1, Per2, Yap1 and Rev-erbα via quantitative real-time PCR. As in A), we will need to synchronise our cells prior RNA collection. In case the expression of the other components of the clock are not affected by YAP-5SA overexpression, we will modify the message of our manuscript to emphasize the role of REV-ERBA. As the referee mentions (and we thank them for that comment), finding that the modulation of Rev-erbα is mechano-sensitive and dependent on YAP/TAZ signalling would be still very relevant, given the role of this factor in metabolism, inflammation, mitochondrial activity, or Alzheimer’s disease, as discussed in lines 231-235 in the manuscript.

1. The authors aim to discard the possibility of paracrine signals by showing no increase in circadian power fraction of cells growing in low density with conditioned medium (Figure 2D). A paracrine signal coming from an oscillatory system is likely to oscillate and in that case, I do not see how growing cells in constant conditional medium can discard the effects of an oscillatory paracrine signal. I believe the elegant experiment shown in Figure 2E more precisely address this issue.

The reviewer is right in the sense that paracrine coupling of circadian oscillators would require a circadian paracrine signal, like shown in Finger et al., 2021, and that we provide sufficient experimental evidence of a mechanics- rather than paracrine-driven control of the RevVNP circadian oscillations. Specifically, by using micropatterning (Fig. 2E) and gap closure (Fig. 2A) we show that cells under the same paracrine medium are able to display acute differences in RevVNP expression. The experiment with conditioned medium, which is a traditional technique used in some papers in the field like in Noguchi et al., 2013, was performed to rule out the possibility that secreted factors, even if not circadian, could ultimately impact the low-density cells’ circadian clock. We will rephrase the manuscript to stress out this reasoning.

Finger AM, Jäschke S, del Olmo M, Hurwitz R, Granada AE, Herzel H & Kramer A (2021) Intercellular coupling between peripheral circadian oscillators by TGF-β signaling. Science Advances 7

Noguchi T, Wang LL & Welsh DK (2013) Fibroblast PER2 circadian rhythmicity depends on cell density. Journal of Biological Rhythms 28: 183–192

Data analysis methodology:

1. Single-cell circadian recordings like the ones analyzed here are characterized by noisy amplitude and non-sinusoidal waveforms with fluctuating period (Bieler et al., 2014; Feillet et al., 2014). The authors interpolate, smooth, detrend and normalize their data; operations that are known to introduce spectral artifacts that can mislead the interpretation of the power spectrum. Moreover, the time-series pre-processing operations described by the authors in the methods sections is incomplete and the authors should more explicitly describe all their operations with exact methods applied, filter parameters and time-windows sizes (if applicable). To validate their pre-processing steps the authors could provide their time-series analysis pipeline code and/or provide a few examples of raw versus pre-processed data together with their respective spectrums before and after pre-processing. In addition, the authors could provide their raw trace signal data together with the corresponding post-processed signal data as plain text files.

In our response to the reviewers, we will address this point exactly as requested by the reviewer. We will rewrite our methods section to explain better our analysis pipeline, clarifying that we do not apply detrending, that we resort rarely to interpolation of missing points, and stating the specifics of the standard low-pass filter we apply. We will then strengthen Supplementary Figure 1 with more examples of raw-data and processed data, and will provide raw trace signal data and the corresponding processed data to illustrate our approach.

1. The authors rely on Fourier analysis and a reasonable self-made definition of circadian strength named as "circadian power fraction". Using a stationary-based method for noisy non-stationary data can lead to inaccurate spectrum power estimations. As the current version of the manuscript does not provide any alternative/complementary analysis method nor we have any available raw signal data it is unclear if their analysis appropriately represents the circadian power. The authors could consider implementing complementary data-analysis strategies to validate their conclusions. Fortunately, there are multiple suitable data analysis strategies already available that are exactly designed for this kind of data (eg. (Price et al., 2008; Leise et al., 2012; Leise, 2013; Bieler et al., 2014; Mönke et al., 2020). This time-series analysis methods is a crucial step as all main results on this manuscript rely on the authors self-made definition of circadian power. This is particularly important as there is no standardized method in the circadian field to estimate circadian rhythmicity and/or circadian power of single-cell traces.

We will take this point into consideration by running a complementary analysis of our data with one of the methods recommended by the reviewer. Our choice is pyBOAT, as presented in Mönke et al. (2020), because on first inspection its implementation of the wavelet method appears to be the most suitable for our dataset type. If we find that our time-series are too short for these methods we will use the RAIN algorithm (Thaben and Westermark, 2014) instead.

Mönke G, Sorgenfrei FA, Schmal C & Granada AE (2020) Optimal time frequency analysis for biological data - pyBOAT Systems Biology

Thaben PF & Westermark PO (2014) Detecting Rhythms in Time Series with RAIN. J Biol Rhythms 29: 391–400

1. The authors mainly show circadian power fraction and analyze rhythmicity scores/powers. Is there the a chance that a rise in the basal expression level of Rev-erbα is reducing the rhythmicity score? Or to phrase it otherwise, the absolute amplitude may remain the same, but the relative amplitude may be reduced? Would that affect the FT analysis power scored? To clarify this the authors could provide an analysis of the relative amplitude in addition to the circadian intensity (as in Fig.1C).

Our analysis pipeline subtracts the mean signal from each cell’s intensity-time trace, and then divides each trace by its standard deviation. This procedure eliminates any bias due to basal expression of Rev-erbα. We will address this point by clarifying the methods section and providing examples in Supplementary Figure 1 of raw data with high-basal levels and low basal levels, showing their pre- and post-processed spectra.

Minor points by text-line:

YAP and TAZ should be introduced to the reader during introduction. by set a of proteins. Here the authors probably meant that cells were not reset nor entrained during the experiment. "..expression depends on..". This is a correlation, not proof of causation is shown until this point. This is an overstatement. Using the term "provoked" suggests a causal relationship not shown. Similarly last sentence "This result established.... is caused..". Again, this is an overstatement as only correlation is shown. According to their description the authors are not using any image-preprocessing steps, eg background subtraction or other filters. Is this correct? It is not clear what image metric for the single-cell signals are the authors using, eg. integrated nuclear intensity or mean/median nuclear intensity. I am not familiar with TrackMate but it might be possible to export and share with the readers the image-analysis pipeline used which would clarify any questions about image processing and signal extraction.

We thank the reviewer for pointing out all these minor points. We will address each one of them to make the paper clearer.

Regarding Reviewer #3:

The authors state in lines 163-165: 'This striking anticorrelation reveals that the robustness of the Rev-erbα circadian expression depends on the nucleocytoplasmic transport of YAP and its mechanosensitive regulation'. Although interesting, the data in figure 3 to which this statement refers is, as the authors identify, correlative, rather than causative. I would strongly suggest altering this statement to better reflect the data.

We will modify the text to eliminate this overstatement.

It looks to me as though all experiments were carried out in the same clonal reporter 3T3 line. To avoid possible issues with founder effects, I would ask that the authors repeat the initial experiment in figure 1B, and the associated analysis as in 1C-E with a different clonal 3T3 line. Hopefully this will not be very arduous, as the methods suggest that multiple clonal 3T3 reporter lines were made initially. With time to defrost, plate, record and analyse the data, I would hope that this would not take more than six weeks maximum.

We will perform the experiments regarding the cell density effect on the RevVNP oscillations (Fig. 1) in another clonal 3T3 line as the reviewer suggests. We have already initiated the experimental repeats with the alternative clone.

I would note that the custom software used for analysis does not appear to be generally available. I would assume that the authors would make this available upon request.

We will extend the explanation of our method as suggested by Reviewer #2 and make the code available to the community.

Experiments appear to have been adequately replicated in terms of n. However, the robustness of these findings would be supported though use of a different clonal reporter line, as discussed above.

We will solve this problem as stated above.

Statistical analysis is generally appropriate. I would suggest including statistical analysis in figures 3B and S4B to demonstrate that the pharmacological treatments are indeed having a statistically significant effect on the MAL and YAP nuclear/cytoplasmic ratio.

We will perform the corresponding statistical analysis on those data.

For Figure 4, it is not stated which statistical tests have been used, with only P values given in table S1. Please state which test has been used.

We will specify the statistical test used in the figure legend.

Furthermore, it would be valuable to see if it is possible to perform statistical analysis looking at the populations should in Figure 4A, to either support or refute the statement made in Line 189-90 that 'we overexpressed 5SA-S94A-YAP, a mutant version of YAP unable to interact with TEAD and observed that the cells recovered, to a large extent, both the RevVNP circadian power fraction and the REV-ERBα basal levels displayed by the wild-type high-density population'

The p-values corresponding to that dataset are represented in Table S1, but we will move them to the figure legend so the extent of the differences between the YAP mutants and the control becomes more noticeable. This applies too to the next comment of the reviewer.

Additionally, it is a little unclear to me why exact p values are reported in table S1. It seems that they might be better placed in the relevant figure legend.

Minor comments:

Although the authors took good care to try to ensure that there was minimal phase synchrony between cells, it would be good to see some analysis to confirm that these efforts were successful. This is of particular concern, given that many things that commonly happen during cell handling, such as temperature change and media change, even with conditioned media, can act to synchronise cells. Hopefully, this information should be available from your existing analysis.

All our experiments, except for the gap closure ones (which imply an unavoidable medium shock after the removal of the gasket where the cells are cultured to achieve high density) are carried out in a similar way (see Materials and Methods). This approach does not involve the typical shock of serum, dexamethasone, or other hormones, because we want to avoid biochemical signalling that could mask the “pure” effect of mechanics on the pathways that affect the circadian clock. In any case, a certain level of synchrony should not affect the analysis we perform, since this is single cell-based and does not consider the phase but the strength of its circadian frequency. But as requested by the reviewer we will analyze the phase signal and report the results if relevant to the project.

It would be informative to see both phase and period analysis for the data shown in figure 2C. Do cells at the edge show differences in relative synchrony following the removal of the PDMS barrier and Rev-erba induction? Is there a period difference between cells at the edge and those that remain confluent?

We agree with the referee that the “shock” received by the cells at the edge should work as a reset of their circadian phase and we have tried to analyse this effect. However, there are technical limitations that make this analysis difficult, mainly the short duration of the experiment and the fact that these cells transition very fast, upon gap closure, from a non-circadian to a circadian behaviour. We will attempt to better report this interesting effect by using the WAVECLOCK (Price et al., 2008) or the pyBOAT method (Mönke et al., 2020), suggested by Reviewer #2, which are designed to analyse non-stationary data.

Mönke G, Sorgenfrei FA, Schmal C & Granada AE (2020) Optimal time frequency analysis for biological data - pyBOAT Systems Biology

Price TS, Baggs JE, Curtis AM, Fitzgerald GA & Hogenesch JB (2008) WAVECLOCK: wavelet analysis of circadian oscillation. Bioinformatics 24: 2794–2795

Figure 2B - the text states that those cells far from the edge oscillate robustly thoughout the experiment, but this is not easy to see from this kymograph due to the dynamic range. Is there another way of presenting this that might make it easier to confirm?

We will calculate the circadian power fraction of the “bulk” cells as we do for the other conditions described in the manuscript. We can also show examples of individual traces if the average shown in Fig. 2C or the kymograph in Fig. 2B are not clear enough.

Figure 1D-E - the text provides periodicity for the high-density cells, but not the low density ones. Could you provide periodicity for both populations - do they differ?

We will represent in more detail the results of the frequency analysis on the low-density cells so the diversity of periods (frequencies) at this condition gets more evident.

Figure S3 - it is interesting to note the difference in population rhythmicity between the bulk and edge data here, which is not seen so clearly in cells without thymidine. Could the authors comment on this?

We agree with the referee that there is an obvious difference regarding RevVNP expression (mainly on the edge cells but also in the bulk) between the experiments with and without thymidine. We hypothesise this is due to the pronounced decrease in cell divisions in the presence of thymidine, which considerably slows down the gap closure and impacts the density of the entire cell population. We will comment this effect in the manuscript.

Line 148 - it is unclear here what is meant by 'the onset of circadian oscillations'. Could you rephrase this for clarity?

We will change that sentence.

Line 173 - a few words to highlight that Lats is a kinase and the function of YAP phosphorylation by Lats would aid clarity here. Similarly, explanation of the functional difference between the protein with 4 Serine to alanine mutations and 5 mutations and why both of these mutants were used would be helpful.

We will clarify this point following the reviewer’s suggestion.

Line 174 - for accuracy, this should perhaps read 'fibroblast circadian clock', as this work is only in 3T3 cells, and therefore may not apply more generally.

We will implement this change.

Line 202 - could you expand to explain the existing limitations of studying cell signalling cascades in synchronised cells? This is not clear to me. Thanks.

We will discuss the signalling effects caused by 50% serum shocks and other traditional ways to synchronise the cells as requested by the reviewer.

Figures 1D and 4B - the choice of colour range used in these kymographs is skewed towards the warmer colours, making it quite hard to discern differences between the groups. I would suggest using the cooler colour range for a greater proportion of the data set, to make rhythmicity, or lack of it, clearer to see.

We will invest further efforts to finding the optimal colour map and range for our datasets.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Abenza et al. investigate an important question of how the physical environment affects the properties of the individual circadian clocks. The authors utilize a set of clever experiments, pharmacological manipulations and data analysis techniques to unveil a potential role of YAP/TAZ in the circadian clock.

Major comments:

Effects on the circadian clock

1. The authors use the fluorescent reporter created by Nagoshi from sections of the Rev-erbα gene. This reporter is widely used to estimate relative circadian timing in individual cells but it does not provide direct information on the circadian clock activity. In other words, while Reverb rhythmic expression is driven by the clock, it is not known whether less-rhythmic or non-rhythmic expression or change in expression level of Rev-erbα is affecting the core clock. For example, it has been shown that Rev-erbα knock-down cells are rhythmic as long as Rev-erb-beta is present. Thus, one major shortcoming of the current version of the manuscript is the missing dissection between Rev-erbα rhythmicity/expression and the circadian clock. More concretely, it remains unclear whether the change in Rev-erbα expression is a direct effect or caused by a defect clock. Since the authors presume a direct effect of YAP/TAP on Rev-erb expression, the former is likely. If that is the case, the data could be interpreted as that (missing) mechanic stimuli can lead to nuclear YAP/TAZ, which rises the level of Rev-erbα (and maybe interfere with its rhythmic accumulation). Beyond Rev-erbα expression, there may or may not be an effect on the circadian clock (core clock, CCGs). With the current version we do not know since the authors do not look beyond Rev-erbα expression. Thus, the claims on circadian clock or circadian rhythms in their cells is not studied in this version of the manuscript. The current version is still very interesting and provides insights into the Rev-erbα modulation, but additional work would be needed to show links with the core clock machinery. For this the authors could show influence (or at least correlation) of the YAP/TAZ/REVERBA phenotype on the oscillations of core clock genes or clock-controlled genes. Either through the use of alternative (ideally constitutive) reporters (e.g. PER2, BMAL1, fluorescent or LUC), or/and by analyzing RNA/Protein of core clock genes or output genes. This would not be necessary for all experiments, but at least for some were its possible (e.g. experiments with drugs perturbations). Otherwise, any claim like "YAP/TAZ perturbs the circadian clock ..." or "the circadian clock deregulation in nuclear YAP-enriched cells" is potentially flawed and has to be removed/reformulated.

2. The authors aim to discard the possibility of paracrine signals by showing no increase in circadian power fraction of cells growing in low density with conditioned medium (Figure 2D). A paracrine signal coming from an oscillatory system is likely to oscillate and in that case, I do not see how growing cells in constant conditional medium can discard the effects of an oscillatory paracrine signal. I believe the elegant experiment shown in Figure 2E more precisely address this issue.

Data analysis methodology:

1. Single-cell circadian recordings like the ones analyzed here are characterized by noisy amplitude and non-sinusoidal waveforms with fluctuating period (Bieler et al., 2014; Feillet et al., 2014). The authors interpolate, smooth, detrend and normalize their data; operations that are known to introduce spectral artifacts that can mislead the interpretation of the power spectrum. Moreover, the time-series pre-processing operations described by the authors in the methods sections is incomplete and the authors should more explicitly describe all their operations with exact methods applied, filter parameters and time-windows sizes (if applicable). To validate their pre-processing steps the authors could provide their time-series analysis pipeline code and/or provide a few examples of raw versus pre-processed data together with their respective spectrums before and after pre-processing. In addition, the authors could provide their raw trace signal data together with the corresponding post-processed signal data as plain text files.

2. The authors rely on Fourier analysis and a reasonable self-made definition of circadian strength named as "circadian power fraction". Using a stationary-based method for noisy non-stationary data can lead to inaccurate spectrum power estimations. As the current version of the manuscript does not provide any alternative/complementary analysis method nor we have any available raw signal data it is unclear if their analysis appropriately represents the circadian power. The authors could consider implementing complementary data-analysis strategies to validate their conclusions. Fortunately, there are multiple suitable data analysis strategies already available that are exactly designed for this kind of data (eg. (Price et al., 2008; Leise et al., 2012; Leise, 2013; Bieler et al., 2014; Mönke et al., 2020). This time-series analysis methods is a crucial step as all main results on this manuscript rely on the authors self-made definition of circadian power. This is particularly important as there is no standardized method in the circadian field to estimate circadian rhythmicity and/or circadian power of single-cell traces.

3. The authors mainly show circadian power fraction and analyze rhythmicity scores/powers. Is there the a chance that a rise in the basal expression level of Rev-erbα is reducing the rhythmicity score? Or to phrase it otherwise, the absolute amplitude may remain the same, but the relative amplitude may be reduced? Would that affect the FT analysis power scored? To clarify this the authors could provide an analysis of the relative amplitude in addition to the circadian intensity (as in Fig.1C).

Minor points by text-line:

1. YAP and TAZ should be introduced to the reader during introduction.
2. by set a of proteins.
3. Here the authors probably meant that cells were not reset nor entrained during the experiment.
4. "..expression depends on..". This is a correlation, not proof of causation is shown until this point. This is an overstatement.
5. Using the term "provoked" suggests a causal relationship not shown.
6. Similarly last sentence "This result established.... is caused..". Again, this is an overstatement as only correlation is shown.
7. According to their description the authors are not using any image-preprocessing steps, eg background subtraction or other filters. Is this correct?
8. It is not clear what image metric for the single-cell signals are the authors using, eg. integrated nuclear intensity or mean/median nuclear intensity. I am not familiar with TrackMate but it might be possible to export and share with the readers the image-analysis pipeline used which would clarify any questions about image processing and signal extraction.

References:

1. Bieler, J, Cannavo, R, Gustafson, K, Gobet, C, Gatfield, D, and Naef, F (2014). Robust synchronization of coupled circadian and cell cycle oscillators in single mammalian cells. Mol Syst Biol 10, 739.

2. Leise, TL (2013). Wavelet analysis of circadian and ultradian behavioral rhythms. J Circadian Rhythms 11, 5.

3. Leise, TL, Wang, CW, Gitis, PJ, and Welsh, DK (2012). Persistent Cell-Autonomous Circadian Oscillations in Fibroblasts Revealed by Six-Week Single-Cell Imaging of PER2::LUC Bioluminescence. PLoS One 7, 1-10.

4. Mönke, G, Sorgenfrei, F, Schmal, C, and Granada, A (2020). Optimal time frequency analysis for biological data - pyBOAT. BioRxiv 179, 985-986.

5. Price, TS, Baggs, JE, Curtis, AM, FitzGerald, GA, and Hogenesch, JB (2008). WAVECLOCK: wavelet analysis of circadian oscillation. Bioinformatics 24, 2794-2795.

Significance

I believe this manuscript is of high significant both for the circadian as well as the mechanobiology fields. Readers from single-cell signalling studies will also be very interested in this work.

To my knowledge the discussed link has not been studied before at single cell level, which as the authors show can provide multiple new insights.

I do work with similar single-cell signals, have broad expertise in microscopy, image analysis methods, time series analysis, and the circadian clock mechanisms but very little experience in mechanobiology.

Drivers run in kernel mode to access the hardware

...and because it's a matter of documentation, it adds to the effort for onboarding. Further slowing down development.

Offline docs: - macOS: Dash ($30) - Windows/Linux: Zeal (free) - Windows: [Velocity] (https://velocity.silverlakesoftware.com/) ($20) - Web: DevDocs

• browser accessible

Schools with stringent masking requirements had far lower rates of transmission, and these weren't even requirements for good masks. In addition, efforts in terms of filtration or ventilation were few and far between, aside from opening windows.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Wang et al. present an evaluation of a new generation of time-of-flight-based mass spectrometer that improves on the fraction of ions factually used for detection of peptide analytes, thus boosting the sensitivity of the Zenotof 7600 system when compared to the same instrument with the duty-cycle-enhancing Zenotrap module disabled and also when compared to the previous generation instrument of the same vendor in some of the comparisons.

The authors position the MS acquisition technique as particularly suitable in combination with medium (micro-) and high ('analytical') flow and throughput methods where higher flow rates (vs. conventional nanoflow-LCMS) allow rapid sample turnover and high throughput, yet limit the efficiency of electrospray and ion transfer into the MS system, thus being in dire need for enhanced sensitivity of the MS system employed for detection. The competency of such an MS system for very low input materials as e.g. encountered in emerging single-cell proteomic workflows, typically employing nanoflow chromatography, was thus not part of the study.

Accordingly, a medium- (micro-flow) and very high ('analytical'-flow) throughput LC method were screened on the three MS (parameter) setups using human cell lysate digests typically utilized in such technical evaluations. Well-received, the authors further extended their analysis (for the new instrument) across additional sample types of clinical and extended biological interest and spanning different levels of complexity and dynamic range of contained protein analytes.

In addition, the authors also performed a controlled ratio 2-species mixture experiment which allows detailed benchmarking of proteome coverage as well as the quality of protein quantification in a known differential comparison for the medium throughput (micro-flow) method.

The data quite convincingly demonstrate an increased sensitivity of the instrument based on similar identification performance in DIA bottom up proteomics from ca. 3- to 8-fold lower input peptide mass. However, I see a number of shortcomings mainly in the presentation and in part the completeness of the work, with specific comments below.

Major comments:

• Are the key conclusions convincing?

  • The concluded 10x sensitivity increase is overstating the observed numbers (x5-x8). In addition, the authors should at least discuss other changes than the Zeno trap incurred in the Zeno SWATH vs non-Zeno-SWATH DIA setups, particularly changes in accumulation times per m/z range, with Zeno Swath accumulating ~42 % longer per cycle spanning the same m/z range (85 vs 60 windows with 11ms per window) in the uflow method set and ~ 18 % longer in the high-flow method set (same window number but 13 ms vs. 11 ms dwell time per window). This should be discussed as one of the optimizations/factors contributing to the increased sensitivity observed in Zeno Swath measurements vs conventional SWATH. On that note, it was unclear to me when and where the 40 variable window SWATH method mentioned in the methods was used and where the settings can be found.
  • Since injected material is a critical parameter here, it would be good if it was mentioned also with the key conclusion on the increased number of confidently quantified peptides in microflow (based on the 2-species controlled quantity experiment).
  • Conclusions 'increasing protein identification numbers through the use of analytical-flow-rate chromatography' does not capture the observed data; the use of analytical-flow-rate does not convey an increase in protein identification numbers but enhanced sensitivity rather enables the maintenance of high protein identification numbers / proteome coverage despite/concurrent with analytical-flow chromatography
  • In titration curve experiments like these, probing proteome coverage from relatively small sample amounts, special care

  • Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

  • 'Zeno SWATH increases protein identification in complex samples<br /> 5- to 10-fold when compared to current SWATH acquisition methods on the same instrument' - At no point this is shown, a decrease of required input amounts by 5-8-fold (increase in sensitivity) is shown by the data, not a multiplication of protein identification rates by that factor.

  • Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

  • Figure 1f, Supplemental Figure 1b, Figure 3 and Supplemental Figure 3 lack data for the Zeno SWATH method's performance at higher concentration. Given the fact that there is a clear, continuous trend of significant enhancement of proteomic depth in the highest 3 concentrations sampled by the Zeno SWATH method, I lack an assessment of the upper limit of proteome coverage achievable by the new platform when input material is not limited, or at least learn why injecting more is not advisable on the ZenoTOF 7600 system. It is clear that the region of interest is the lower loads where sensitivity gains are most pronounced, but with the strong trend in IDs per ng injected in the sampled range and discrepant range sampled by the non-Zeno method I feel there is a gap in the dataset and the upper ceiling of proteome coverage could be mapped out more thoroughly (At least for human cell lysate and possibly human plasma where trends appear most (log2-)linear).

  • Similarly, unless constrained for technical or practical reasons, I would suggest to find the ceiling for achievable proteome depth in analytical flow (4, 8 ug?)

  • Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

  • All these should be re-injections of existing samples on these MS setups and a minor effort provided instrument availability (<1w) and rapid re-analysis via DIA-NN.

  • Are the data and the methods presented in such a way that they can be reproduced?

  • The raw data have not been deposited to a public repository. Reproducibility of the study would benefit significantly by raw data (including search results and spectral libraries with log files of creation) upload/sharing e.g. via ProteomeXchange/PRIDE.

  • If any software versions or firmwares on the hardware are required to perform the measurements on the ZenoTOF on the market today, these versions and prospective release dates should be included or the accessibility of these settings commented on.

  • Are the experiments adequately replicated and statistical analysis adequate?

  • Figures 3 and Supplemental Figure 3 need a clarification in the legend as to the nature and origin of ID numbers (mean? Number of replicates? Add error bars if possible)

  • The usage of DIA-NN for data analysis is somewhat unclear, in particular the in Methods/Spectral libraries "For the analysis of plasma samples, a project-independent public spectral library [29] was used as described previously [15]. The Human UniProt [30] isoform sequence database (UP000005640, 19 October 2021) was used to annotate the library and the processing was performed using the MBR mode in DIA-NN." The authors should address in a revised version whether the identification numbers reported stem from two-pass or single-pass analysis (i.e. when the feature termed Match-between-runs implemented since DIANNv1.8 was enabled and whether all runs, spanning different injection amounts were co-analyzed and data-re-queried for a targeted library containing precursors identified in high load samples in first pass analysis and then queried in low-load samples. In other words, are the low-load IDs independent of high load IDs? If not (i.e. the different loads were co-analyzed with MBR), what proteome coverage to the low sample loads reach bona fide, without the 'guidance' of high-load IDs?

Side note: Turning this around, could a high-load injection e.g. from a pool of limited-amount samples serve as a guiding element in a MBR-enabled analysis of a large cohort with limited sample amounts available per biological condition?

Minor comments:

• Specific experimental issues that are easily addressable.

  • The authors state the impact on dynamic range of identification when comparing ID sets against an external dataset with presumable cellular concentration numbers. I would in addition suggest comparing the dynamic range of the quantititative values observed from the available data which should provide a direct assessment of the dynamic range of quantification of the two methods.

  • Are prior studies referenced appropriately?

  • The statement that conventional DIA methods rely on nanoflow chromatography (p3, paragraph 3) is not accurate as there is previous implementations of data-independent acquisition MS of microflow separations, in part the group's work and referred to later in the text.

o Vowinckel, J. et al. Cost-effective generation of precise label-free quantitative proteomes in high-throughput by microLC and data-independent acquisition. Sci. Rep. 8, 4346 (2018)

o Bruderer, R. et al. Analysis of 1508 plasma samples by capillary-flow data-independent acquisition profiles proteomics of weight loss and maintenance. Mol. Cell Proteom. 18, 1242-1254 (2019).

It is correct that most early implementations of DIA-MS utilized nanoflow separations due to sensitivity and proteome coverage but DIA as such is a chromatography-flow-speed-agnostic principle and the concept to combine microflow LC with DIA not new, yet powerful as demonstrated by the authors and others previously and once again, here. - P.3 paragraph 3 'Moreover, the increased sensitivity of DIA methods has facilitated applications in large-scale proteomics, including system-biology studies in various model organisms, disease states, and species [5-9]' Include Ref 4 where improved sensitivity of DIA was demonstrated (at proteomic breadth..) - Are the text and figures clear and accurate?

-   Text and Figures need to be edited for typos, language, and clarity/accuracy.

1. Abstract 'Zeno SWATH increases protein identification in complex samples<br /> 5- to 10-fold when compared to current SWATH acquisition methods on the same instrument' - At no point this is shown, a drop of required input amounts by 5-8-fold (increase in sensitivity) is shown by the data, not a multiplication of protein identification rates.
2. P. 4 paragraph 3: Use terms 'consensus' or 'shared' identifications or similar to refer to the proteins identified in all 3 replicates, rather than 'reproducible' when discussing the reproducibility of peptide and protein quantification (as contrast to reproducibility of identification).
3. P.3 paragraph 2 'selects and fragments multiple charge ions' -> multiply charged (?)
4. P. 4 p. 1 'leading to under-detection' please clarify (leading to partial ion usage and limited sensitivity?)
5. P. 6 paragraph 3 'The gain in identification number of Zeno SWATH versus SWATH is mostly explained by an increased dynamic range: i.e. more low-abundance proteins are detected' - Reformulate/clarify: Is increased dynamic range of identifications against external quantities an explanation or perhaps simply the increased sensitivity with improved duty cycle?
6. Term 'active gradient' unclear. An inactive gradient is isocratic flow. Omit 'active'. Isocratic/other portions are overhead.
7. Figure 1 panel a) iteration scheme a-d) is redundant with the rest of the figure; use alternative iter scheme within panel a). Panel a) is further contains illegibly small fonts and should be edited for legibility
8. Revisit y-axis labels. Example: Fig. 1f) 'Precursors Identificaiton' -> Precursors identified/Precursor identifications. Correct throughout manuscript
9. ID bar graphs in all Figures: Cumulative IDs shade of grey is not properly visible, suggest alternate color scheme or add black color outline to the bars
10. Figure 1 e) legend 'along gradient length' -> gradient time / retention time
11. Figure 1 d) too small, trend lines mentioned in text invisible in graph. Boxplots very small.
12. There is three different terms used for the high throughput method (analytical-flow, high-flow, and another one.. please align where possible for clarity (i.e. choose 2 names for the 2 methods throughout the manuscript) etc..

13. Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

    • They authors may consider adding a short explanation of the term 'dynamic range coverage of identification' to contrast this from a direct assessment of dynamic range of quantitative values observed in this study.
    • 2-species controlled experiment: The discrepancy of observed vs true mixing ratios suggests the data were scaled during the analysis which, with these mixture ratios, tends to distort the accuracy (i.e. generates offset of observed from true ratio. That's very likely not a pipetting error on a log scale). In other words, you may want to evaluate the raw quantitative ratios (w/o any normalization/scaling applied) which should be more reflective of true/manual pipetting ratios in light of normalization strategy incompatibily with certain species mix scenarios (compare Supplementary Figure 1 a). Note to the editor(s): This will not affect the clear benefit of Zenotrap usage demonstrated by the 2-species benchmark as is but can be considered a minor yet recommended improvement (thus here).
    • The 2-species controlled experiment can reveal more information than currently extracted and I would recommend to show Zeno Swath and Swath xy scatters, including count-scaled density distributions of the observed ratios, side-by side. This would give deeper understanding of the large impact of the Zeno SWATH method. Also, I believe I haven't seen any instrument to date delivering precise quantification over as broad a dynamic range as surmisable from Fig. 1d) which might be worth wile highlighting.

Significance

Wang et al. describe a technical advance in ion usage and sensitivity based on an ion-trap device storing and focusing ions for TOF-based bottom-proteomics measurements. The study demonstrates improved sensitivity relative to previous generation instrumentation and also explores the impact of the specific trap device relative to the general improvements of the remaining MS system. The work outlines a route towards high coverage proteomics at very high throughput and robustness, as desirable in clinical proteomics and prospective personalized medicine approaches. While not all sample types of interest are limited to the amounts where the strongest improvements are seen in the presented data, large scale studies across expansive cohorts will likey be rendered more practical and realistic due to reduced instrument contamination at reduced loads and also further applications beyond those discussed in the manuscript will be rendered feasible on the newer generation instrument.

The improved ZenoTOF system and SWATH method follows a series of innovations in the mass spectrometry instrumentation, most notably and related the drastic improvement of ion utilization by storage e.g in a trapped ion mobility device earlier in the ion stream where, beyond an accumulation-based boost of sensitivity, ion mobility as a further biophysical properties is assessed in addition to the conventional m/z, as reviewed recently (doi: 10.1016/j.mcpro.2021.100138.). While these developments culminated and have been targeting low-flow, ultra-high sensitivity applications such as single-cell proteomics, the present study takes a different angle towards higher throughput measurements from significantly larger than single cell, but also significantly lower than historically required sample amounts that were prohibitive to a range of applications that are now easier to accomplish thanks to this and related work of the authors and others. The presented research appears of broad relevance and interest to the scientific community interested in protein abundance pattern analysis, in particular in larger (clinical) cohorts. Furthermore, the performance metrics on proteomic depth from human cell lysate digests will likely allow researchers with analytical quests other than those exemplified in the manuscript to extrapolate the ZenoTOF and Zeno SWATH suitability for their respective analytical targets.

Reviewer Field of expertise/background:

Quantitative proteomics. DIA mass spectrometry method & algorithm development & heavy usage. Protein Biochemistry. Molecular Biology.

Window effect depends on the absolute phase (type of substrate: oxide or metal). Thus sample substrate has to be used. For non-ideal windows it also depends on the ambient. From my point of view, window effect should best be defined with the correct reference substrate within the ambient of the subsequent sample measurement.

Reviewer #3 (Public Review):

In this work, Dumrongprechachan et al. impressively expanded their earlier work on the identification of cell type-specific subcellular proteomes from mouse brain by APEX2 proximity labeling. Instead of using viral expression of APEX2, the authors now created a Cre-dependent APEX2 reporter mouse line using CRISPR knock-in, which can be combined with multiple Cre-driver lines for proteomic applications. Using this novel tool in combination with sophisticated mass spectrometry and elegant bioinformatics, they mapped the temporal dynamics of the axonal proteome in corticostriatal projections (instead of only identifying a static cell type- and compartment-specific proteome) together with its phosphorylation status (instead of only looking at protein abundance). The data will provide a valuable resource on developmental trajectories at the proteomic and phosphoproteomic level, and will allow for pathway- and phosphosite-centric systems-level analyses as exemplified by the identification of proline-directed protein kinases as major regulators of corticostriatal projection development.

Strengths:<br /> The key tool developed in this work is the APEX2 reporter mouse line as it enables capturing of early postnatal time points, which was not possible before due to the time window of 2-4 weeks required for viral APEX expression. Thus, this tool puts the authors into position to access the temporal dynamics of the developing axon at time points spanning from neonate (as early as P5) to young adult (P50). Within this complex experimental design, the authors even managed to introduce a crucial compartment control at least for the time point P18, in which APEX expression is restricted to nucleus and soma upon viral expression. The resulting resource will be of high value as the data are derived from advanced mass spectrometric methods and stringent data handling. Examples of this high level of scrutiny include the use of MS3 methodology for the acquisition of TMT data to address the ratio distortion issues typically seen with isobaric labeling and thereby increase the quantification accuracy and the limitation to proteins quantified in all biological replicates.

Weaknesses:<br /> As to sample preparation for mass spectrometry, the authors follow the interesting concept of first enriching the phosphopeptides from the pool of TMT-labeled tryptic peptides and then using the unbound fraction from that step for further peptide fractionation, followed by mass spectrometric protein quantification. While this strategy sounds very straightforward in principle, one would expect that the phosphopeptide enrichment comes with an unspecific loss of other peptides in general, and with a semi-specific loss of acidic peptides in particular. Was this potential issue investigated by comparison with samples that were fractionated directly without prior phosphopeptide enrichment? Or with other words: the rationale for this sequential procedure is compelling - quantification of both protein and phosphopeptide abundance from the same (limited) sample, but what is the price for it as to peptide loss?

The APEX2 reporter mouse line is a novel tool with broad applicability for proximity labeling approaches and, understandably, the authors advertise its advantages, mainly via the suitability for short temporal windows. However, the discussion on the limitations of the approach falls short. The authors should make clear that the APEX method in general is limited to ex vivo approaches such as the acute brain slices used here due to the limitation that potentially toxic reagents (i.e. low membrane-permeable biotin-phenol and H2O2) have to be delivered to the target tissue. Although treatment with H2O2 is rather short, undesired oxidative stress signaling may have to be taken into account, particularly when protein phosphorylation rather than protein abundance is assessed. It would also be interesting to discuss the pros and cons of perfusing the mice prior to preparation of brain slices; e.g., in the context of removal of catalases/endogenous peroxidases or potential for substrate delivery (like recently shown in heart, doi: 10.1038/s41586-020-1947-z). Another issue with the Discussion is that the authors do not properly reflect the involvement of proline-directed kinases in the development of corticostriatal projections, which stands in contrast to the fact that they sell this as one of their major findings throughout the manuscript, including the Abstract.