Author response:

Reviewer #1 (Public review):

Summary:

Loh and colleagues investigate valence encoding in the mesolimbic dopamine system. Using an elegant approach, they show that sucrose, which normally evokes strong dopamine neuron activity and release in the nucleus accumbens, is made aversive via conditioned taste aversion, the same sucrose stimulus later evokes much less dopamine neuron activity and release. Thus, dopamine activity can dynamically track the changing valence of an unconditioned stimulus. These results are important for helping clarify valence and value related questions that are the matter of ongoing debate regarding dopamine functions in the field.

Strengths:

This is an elegant way to ask this question, the within subject's design and the continuity of the stimulus is a strong way to remove a lot of the common confounds that make it difficult to interpret valence-related questions. I think these are valuable studies that help tie up questions in the field while also setting up a number of interesting future directions. There are number of control experiments and tweaks to the design that help eliminate a number of competing hypotheses regarding the results. The data are clearly presented and contextualized.

Weaknesses for consideration:

The focus on one relatively understudied region of the rat striatum for dopamine recordings could potentially limit generalization of the findings. While this can be determined in future studies, the implications should be further discussed in the current manuscript.

We agree that the manuscript would benefit from providing a stronger rationale for our recording sites and acknowledging the potential for regional differences in dopamine signaling. We have made the following additions to the manuscript:

Added to the Discussion: “Recordings were targeted to the lateral VTA and the corresponding approximate terminal site in the NAc lateral shell (Lammel et al., 2008). Subregional differences in dopamine activity likely contribute to mixed findings on dopamine and affect. For example, dopamine in the NAc lateral shell differentially encodes cues predictive of rewarding sucrose and aversive footshock, which is distinct from NAc medial shell dopamine responses (de Jong et al., 2019). Our findings are similar to prior work from our group targeting recordings to the NAc dorsomedial shell (Hsu et al., 2020; McCutcheon et al., 2012; Roitman et al., 2008): there, intraoral sucrose increased NAc dopamine release while the response in the same rats to quinine was significantly lower.”

Reviewer #2 (Public review):

Summary:

Koh et al. report an interesting manuscript studying dopamine binding in the lateral accumbens shell of rats across the course of conditioned taste aversion. The question being asked here is how does the dopamine system respond to aversion? The authors take advantage of unique properties of taste aversion learning (notably, within-subjects remapping of valence to the same physical stimulus) to address this.

They combine a well controlled behavioural design (including key, unpaired controls) with fibre photometry of dopamine binding via GrabDA and of dopamine neuron activity by gCaMP, careful analyses of behaviour (e.g., head movements; home cage ingestion), the authors show that, 1) conditioned taste aversion of sucrose suppresses the activity of VTA dopamine neurons and lateral shell dopamine binding to subsequent presentations of the sucrose tastant; 2) this pattern of activity was similar to the innately aversive tastant quinine; 3) dopamine responses were negatively correlated with behavioural (inferred taste reactivity) reactivity; and 4) dopamine responses tracked the contingency of between sucrose and illness because these responses recovered across extinction of the conditioned taste aversion.

Strengths:

There are important strengths here. The use of a well-controlled design, the measurement of both dopamine binding and VTA dopamine neuron activity, the inclusion of an extinction manipulation; and the thorough reporting of the data. I was not especially surprised by these results, but these data are a potentially important piece of the dopamine puzzle (e.g., as the authors note, salience-based argument struggles to explain these data).

Weaknesses for consideration:

(1) The focus here is on the lateral shell. This is a poorly investigated region in the context of the questions being asked here. Indeed, I suspect many readers might expect a focus on the medial shell. So, I think this focus is important. But, I think it does warrant greater attention in both the introduction and discussion. We do know from past work that there can be extensive compartmentalisation of dopamine responses to appetitive and aversive events and many of the inconsistent findings in the literature can be reconciled by careful examination of where dopamine is assessed. I do think readers would benefit from acknowledgement this - for example it is entirely reasonable to suppose that the findings here may be specific to the lateral shell.

As with our response to Reviewer 1, we agree that we should provide further rationale for focusing our recordings on the lateral shell and acknowledge potential differences in dopamine dynamics across NAc subregions. In addition to the changes in the Discussion detailed in our response to Reviewer 1, we have made the following additions to the Introduction:

Added to the Introduction: “NAc lateral shell dopamine differentially encodes cues predictive of rewarding (i.e., sipper spout with sucrose) and aversive stimuli (i.e., footshock), which is distinct from other subregions (de Jong et al., 2019). It is important to note that other regions of the NAc may serve as hedonic hotspots (e.g. dorsomedial shell; or may more closely align with the signaling of salience (e.g. ventromedial shell; (Yuan et al., 2021)).”

(2) Relatedly, I think readers would benefit from an explicit rationale for studying the lateral shell as well as consideration of this in the discussion. We know that there are anatomical (PMID: 17574681), functional (PMID: 10357457), and cellular (PMID: 7906426) differences between the lateral shell and the rest of the ventral striatum. Critically, we know that profiles of dopamine binding during ingestive behaviours there can be highly dissimilar to the rest of ventral striatum (PMID: 32669355). I do think these points are worth considering.

There are several reasons why dopamine dynamics were recorded in the NAc lateral shell:

(1) Dopamine neurons in more medial aspects of the VTA preferentially target the NAc medial shell and core whereas dopamine neurons in the lateral VTA – our target for VTA DA recordings – project to the lateral shell of the NAc (Lammel et al., 2008). Thus, our goal was to sample NAc release dynamics in areas that receive projections from our cell body recording sites.

(2) Cues predictive of reward availability (i.e., sipper spout with sucrose) and aversive stimuli (i.e., footshock) are differentially encoded by NAc lateral shell dopamine, which is distinct from NAc ventromedial shell dopamine responses (de Jong et al., 2019). These findings suggest a role for NAc lateral shell dopamine in the encoding of a stimulus’s valence, which made the subregion an area of interest for further examination.

(3) With respect to the medial NAc shell specifically, extensive literature had already shown it to be a ‘hedonic hotspot’ (Morales and Berridge, 2020; Yuan et al., 2021) whereas the ventral portion is more mixed with respect to valence (Yuan et al., 2021). We had previously shown that intraoral infusions of primary taste stimuli of opposing valence (i.e., sucrose and quinine) evoke differential responses in dopamine release within the NAc dorsomedial shell (Roitman et al., 2008). We more recently replicated differential dopamine responses from dopamine cell bodies in the lateral VTA (Hsu et al., 2020) and thus endeavored to the possibility of changing dopamine responses in the lateral VTA to the same stimulus as its valence changes. As a result of these choices, measuring dopamine release in the lateral shell was a logical choice. The field would greatly benefit from continued future work surveying the entirety of the VTA DA projection terminus. 

We have included these points of justification in the Introduction and Discussion sections.

(3) I found the data to be very thoughtfully analysed. But in places I was somewhat unsure:

(a) Please indicate clearly in the text when photometry data show averages across trials versus when they show averages across animals.

We have now explicitly indicated in the figure legends of Figures 1, 3, 5, 7, and 8:

(1) In heat maps, each row represents the averaged (across rats) response on that trial.

(2) Traces below heat maps represent the response to infusion averaged first across trials for each rat and then across all rats.

(3) Insets represent the average z-score across the infusion period averaged first across all trials for each rat and then across all rats.

(b) I did struggle with the correlation analyses, for two reasons.

(i) First, the key finding here is that the dopamine response to intraoral sucrose is suppressed by taste aversion. So, this will significantly restrict the range of dopamine transients, making interpretation of the correlations difficult.

The overall hypothesis is that the dopamine response would correlate with the valence of a taste stimulus – even and especially when the stimulus remained constant but its valence changed. We inferred valence from the behavioral reactivity to the stimulus – reasoning that an appetitive taste will evoke minimal movement of the nose and paws (presumably because the animals are primarily engaging in small mouth movements associated with ingestion as shown by the seminal work of Grill and Norgren (1978) and the many studies published by the K.C. Berridge group) whereas an aversive taste will evoke significantly more movement as the rats engage in rejection responses (e.g. forelimb flails, chin rubs, etc.). When we conducted our regression analyses we endeavored to be as transparent as possible and labeled each symbol based on group (Unpaired vs Paired) and day (Conditioning vs Test). Both behavioral reactivity and dopamine responses change – but only for the Paired rats across days. In this sense, we believe the interpretation is clear. However, the Reviewer raises an important criticism that there would essentially be a floor effect with dopamine responses. We believe this is mitigated by data acquired across extinction and especially in Figure 9B. Here, the observations that dopamine responses fall to near zero but return to pre-conditioning levels in the Paired group with strong correlation between dopamine and behavioral reactivity throughout would hopefully partially allay the Reviewer’s concerns. See Part ii below for further support.

(ii) Second, the authors report correlations by combining data across groups/conditions. I understand why the authors have done this, but it does risk obscuring differences between the groups. So, my question is: what happens to this trend when the correlations are computed separately for each group? I suspect other readers will share the same question. I think reporting these separate correlations would be very helpful for the field -

regardless of the outcome.

To address this concern, we performed separate regression analyses for Paired and Unpaired rats and provide the table below to detail results where data were combined across groups or separated. Expectedly, all analyses in Paired rats indicated a significant inverse relationship between dopamine and behavioral reactivity. Afterall, it is only in this group where behavioral reactivity to the taste stimulus changes as function of conditioning. Perhaps even more striking is that in almost all comparisons, even when restricting the regression analysis to Unpaired rats, we still observed a significant inverse relationship between dopamine and behavioral reactivity in most experiments. We have outlined the separated correlations below (asterisks denote slopes significantly different from 0; * p<0.05; ** p<0.01; *** p<0.005; **** p<0.001):

Author response table 1.

(4) Figure 1A is not as helpful as it might be. I do think readers would expect a more precise reporting of GCaMP expression in TH+ and TH- neurons. I also note that many of the nuances in terms of compartmentalisation of dopamine signalling discussed above apply to ventral tegmental area dopamine neurons (e.g. medial v lateral) and this is worth acknowledging when interpreting t

Others have reported (Choi et al., 2020) and quantified (Hsu et al., 2020) GCaMP6f expression in TH+ neurons. While we didn’t report these quantifications, our observations were very much in line with previous quantifications from our laboratory (Hsu et al. 2020).

We agree that we should elaborate on VTA subregional differences and have answered this response above (See responses to Reviewer 1 Weakness #1 and Reviewer 2 Weakness #2).

Reviewer #3 (Public review):

Summary:

This study helps to clarify the mixed literature on dopamine responses to aversive stimuli. While it is well accepted that dopamine in the ventral striatum increases in response to various rewarding and appetitive stimuli, aversive stimuli have been shown to evoke phasic increases or decreasing depending on the exact aversive stimuli, behavioral paradigm, and/or dopamine recording method and location examined. Here the authors use a well-designed set of experiments to show differential responses to an appetitive primary reward (sucrose) that later becomes a conditioned aversive stimulus (sucrose previously paired with lithium chloride in a conditioned taste aversion paradigm). The results are interesting and add valuable data to the question of how the mesolimbic dopamine system encodes aversive stimuli, however, the conclusions are strongly stated given that the current data do not necessarily align with prior conflicting data in terms of recording location, and it is not clear exactly how to interpret the generally biphasic dopamine response to the CTA-sucrose which also evolves over exposures within a single session.

Strengths:

• The authors nicely demonstrate that their two aversive stimuli examined, quinine and sucrose following CTA, evoked aversive facial expressions and paw movements that differed from those following rewarding sucrose to support that the stimuli experienced by the rats differ in valence.

• Examined dopamine responses to the exact same sensory stimuli conditioned to have opposing valences, avoiding standard confounds of appetitive and aversive stimuli being sensed by different sensory modalities (i.e., sweet taste vs. electric shock)

• The authors examined multiple measurements of dopamine activity - cell body calcium (GCaMP6f) in midbrain and release in NAc (Grab-DA2h), which is useful as the prior mixed literature on aversive dopamine responses comes from a variety of recording methods.

• Correlations between sucrose preference and dopamine signals demonstrate behavioral relevance of the differential dopamine signals.

• The delayed testing experiment in Figure 7 nicely controls for the effect of time to demonstrate that the "rewarding" dopamine response to sucrose only recovers after multiple extinction sucrose exposures to extinguish the CTA.

Weaknesses for consideration:

(1) Regional differences in dopamine signaling to aversive stimuli are mentioned in the introduction and discussion. For instance, the idea that dopamine encodes salience is strongly argued against in the discussion, but the paper cited as arguing for that (Kutlu et al. 2021) is recording from the medial core in mice. Given other papers cited in the text about the regional differences in dopamine signaling in the NAc and from different populations of dopamine neurons in midbrain, it's important to mention this distinction wrt to salience signaling. Relatedly, the text says that the lateral NAc shell was targeted for accumbens recordings, but the histology figure looks like the majority of fibers were in the anterior lateral core of NAc. For the current paper to be a convincing last word on the issue, it would be extremely helpful to have similar recordings done in other parts of the NAc to do a more thorough comparison against other studies.

As the Reviewer notes, NAc dopamine recordings were aimed at the lateral NAc shell. It is possible that some dopamine neurons lying within the anterior lateral core were recorded. Fiber photometry and the size of the fiber optics cannot definitively identify the precise location and number of dopamine neurons from which we recorded. Still, recording sites did not systematically differ between groups. Further, the within-subjects design helps to mitigate any potential biases for one subregion over another. The results presented in the manuscript strongly support a valence code. It is difficult to be the ‘last word’ on this topic and we suspect debate will continue. We used taste stimuli for appetitive and aversive stimuli – whereas many in the field will continue to use other noxious stimuli (e.g. foot shock) that likely recruit different circuits en route to the VTA. And there may very well be a different regional profile for dopamine signaling with different noxious stimuli. Moreover, we used intraoral infusion to avoid confounds of stimulus avoidance and competing motivations (e.g. food or fluid deprivation). We believe that this is one of the most important and unique features of our report. Recent work supports a role for phasic increases in dopamine in avoidance of noxious stimuli (Jung et al., 2024) and it will be critical for the field to reflect on the differences between avoidance and aversion. Moreover, in ongoing studies we aspire to fully survey dopamine signaling in conditioned taste aversion across the medial-lateral and dorsal-ventral axes of the VTA and NAc.

(2) Dopamine release in the NAc never dips below baseline for the conditioned sucrose. Is it possible to really consider this as a signal for valence per se, as opposed to it being a weaker response relative to the original sucrose response?

Indeed, NAc dopamine release to intraoral quinine nor aversive sucrose doesn’t dip below baseline but rather dopamine binding doesn’t change from pre-infusion baseline levels. It should be noted that VTA dopamine cell body activity does indeed dip below baseline in response to aversive sucrose. Moreover, using fast-scan cyclic voltammetry, we showed that dopamine release dips below baseline in the NAc dorsomedial shell in response to intraoral quinine (Roitman et al., 2008). The differences across recording sites may reflect regional differences but they may also reflect differences in recording approaches. GrabDA2h, used here, has relatively slow kinetics that may obscure dips below baseline (see response Weakness# 8 below).

(3) Related to this, the main measure of the dopamine signal here, "mean z-score," obscures the temporal dynamics of the aversive dopamine response across a trial. This measure is used to claim that sucrose after CTA is "suppressing" dopamine neuron activity and release, which is true relative to the positive valence sucrose response. However, both GRAB-DA and cell-body GCaMP measurements show clear increases after onset of sucrose infusion before dipping back to baseline or slightly below in the average of all example experiments displayed. One could point to these data to argue either that aversive stimuli cause phasic increases in dopamine (due to the initial increase) or decreases (due to the delayed dip below baseline) depending on the measurement window. Some discussion of the dynamics of the response and how it relates to the prior literature would be useful.

We have used mean z-score to do much of our quantitative analyses but the Reviewer raises the intriguing possibility that we are masking an initial increase in dopamine release and VTA DA activity evoked by aversive taste by doing so. We included the heat maps in the manuscript to be as transparent as possible about the time course of dopamine responses – both within a trial and across trials. The Reviewer’s point prompted us to reflect further on the heat maps and recognize that trials early in the session often showed a brief increase in dopamine for aversive sucrose but this response dissipated (NAc dopamine release) or flipped (VTA DA cell body activity) over trials. We now quantitatively characterize this feature by looking at the timecourse of dopamine responses in each third of the trials (1-10, 11-20, 21-30; see Author response images 1,2 and 3). As we infer the valence of the stimulus from nose and paw movements (behavioral reactivity), it is especially striking that we a similar timecourse for changes in behavior. Collectively, the data may reflect an updating process that is relatively slow and requires experience of the stimulus in a new (aversive) state – that is, a model-free process. While our experiments were not designed to test the updating of dopamine responses and discern their participation in model-based versus model-free learning processes – another debate in the dopamine field (Cone et al., 2016; Deserno et al., 2021)– the data reflect a model-free process. This is further supported in the experiment involving multiple conditioning sessions, where dopamine ‘dips’ are observed in trials 1-10 on Conditioning Day 3 and Extinction Day 1 when the new value of sucrose has been established. Finally, the relatively slow updating of the value of sucrose is reflected in older literature using a continuous intraoral infusion. Using this approach, rats began rejecting the saccharin infusion only after ~2min rather than immediately (Schafe et al., 1998; Schafe and Bernstein, 1996; Wilkins and Bernstein, 2006).   

Author response image 1.

Author response image 2.

Author response image 3.

(4) Would this delayed below-baseline dip be visible with a shorter infusion time?

While our experiments did not explore this parameter, it would be interesting to parametrically vary infusion duration times and examine differences in dopamine responses. However, we believe the most parsimonious explanation is that the ‘dip’ in VTA cell body activity develops as a function of the slow updating of the value of sucrose reflective of a model-free process. We recognize that this is mere speculation.

(5) Does the max of the increase or the dip of the decrease better correlate with the behavioral measures of aversion (orofacial, paw movements) or sucrose preference than "mean z-score" measure used here?

It seems plausible that finding the most extreme value from baseline could better correlate to behavioral measures. Time courses to max increase and max decrease are different. Moreover, with appetitive sucrose, there are often multiple transients that occur throughout a single intraoral infusion. Coupled with a noisy time course for individual components of behavioral reactivity, we determined that averaging data across the whole infusion period (i.e. mean z-score) was the most objective way we could analyze the dopamine and behavioral responses to taste stimuli.

(6) The authors argue strongly in the discussion against the idea that dopamine is encoding "salience." Could this initial peak (also seen in the first few trials of quinine delivery, fig 1c color plot) be a "salience" response?

Our response above to the potential for ‘mixed’ dopamine responses to aversive sucrose led to additional analyses that support a slow updating of both behavior and dopamine to the new, aversive value of sucrose. Quinine is innately aversive and thus the Reviewer rightly points out that even here we observe an increase in dopamine release evoked by quinine on the first few trials (as observed in the heat map). We’d like to note, though, that the order of stimulus exposure was counterbalanced across rats. In those rats first receiving a sucrose session, quinine initially caused a modest increase in dopamine release during the first 10 trials (which is more pronounced in the first 2 trials). In the subsequent 2 blocks of 10 trials, no such increase was observed. Interestingly, in rats for which quinine was their first stimulus, we did not see an increase in dopamine release on the first few trials (see Author response image 4). We speculate that the initial sucrose session required the value of intraoral infusions to be updated when quinine was delivered to these rats and that, once more, the updating process may be slow and akin to a model-free process. This analysis, at present, is underpowered but will direct future attention in follow-up work.

Author response image 4.

(7) Related to this, the color plots showing individual trials show a reduction in the increases to positive valence sucrose across conditioning day trials and a flip from infusion-onset increase to delayed increases across test day trials. This evolution across days makes it appear that the last few conditioning day trials would be impossible to discriminate from the first few test day trials in the CTA-paired. Presumably, from strength of CTA as a paradigm, the sucrose is already aversive to the animals at the first trial of test day. Why do the authors think the response evolves across this session?

As the Reviewer noted, Points 3-7 are related. We have speculated that the evolving dopamine response in Paired rats across test day trials reflects a model-free process. Importantly, as in the manuscript, our additional analyses once again show a tight relationship between behavioral reactivity and the dopamine response across the test session trials. It is important to note, though, that these experiments were not designed to test if responses reflect model-free or model-based processes.

(8) Given that most of the work is using a conditioned aversive stimulus, the comparison to a primary aversive tastant quinine is useful. However, the authors saw basically no dopamine response to a primary aversive tastant quinine (measured only with GRAB-DA) and saw less noticeable decreases following CTA for NAc recordings with GRAB-DA2h than with cell body GCaMP. Given that they are using the high-affinity version of the GRAB sensor, this calls into question whether this is a true difference in release vs. soma activity or issue of high affinity release sensor making decreases in dopamine levels more difficult to observe.

We share the same speculation as the Reviewer. Using fast-scan cyclic voltammetry, albeit measuring dopamine concentration in the dorsomedial shell, we observed a clear decrease from baseline with intraoral infusions of quinine (Roitman et al., 2008). Using fiber photometry here, the Reviewer and we note that GRAB_DA2h is a high-affinity (i.e., EC50: 7nM) dopamine sensor with relatively long off-kinetics (i.e., t1/2 decay time: 7300ms) (Labouesse et al., 2020). It may therefore be much more difficult to observe decreases (below baseline) using this sensor. The publication of new dopamine sensors - with lower affinity, faster kinetics, and greater dynamic range (Zhuo et al., 2024) – introduces opportunities for comparison and the greater potential for capturing decreases below baseline. Due to the poorer kinetics associated with GRAB_DA2h, we would not assert that direct comparisons between the GCaMP- and GRAB-based signals observed here represent true differences between somatic and terminal activity.

References

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Author response:

Responses to Editors:

We appreciate Reviewer 1’s first concern regarding the difficulty of disentangling the contributions of tightly-coupled brain regions to the speech-gesture integration process—particularly due to the close temporal and spatial proximity of the stimulation windows and the potential for prolonged disruption. We would like to provide clarification and evidence supporting the validity of our methodology.

Our previous study (Zhao et al., 2021, J. Neurosci) employed the same experimental protocol—using inhibitory double-pulse transcranial magnetic stimulation (TMS) over the inferior frontal gyrus (IFG) and posterior middle temporal gyrus (pMTG) in one of eight 40-ms time windows. The findings from that study demonstrated a time-window-selective disruption of the semantic congruency effect (i.e., reaction time costs driven by semantic conflict), with no significant modulation of the gender congruency effect (i.e., reaction time costs due to gender conflict). This result establishes that double-pulse TMS provides sufficient temporal precision to independently target the left IFG and pMTG within these 40-ms windows during gesture-speech integration. Importantly, by comparing the distinctively inhibited time windows for IFG and pMTG, we offered clear evidence of distinct engagement and temporal dynamics between these regions during different stages of gesture-speech semantic processing.

Furthermore, we reviewed prior studies utilizing double-pulse TMS on structurally and functionally connected brain regions to explore neural contributions across timescales as brief as 3–60 ms. These studies, which encompass areas from the tongue and lip areas of the primary motor cortex (M1) to high-level semantic regions such as the pMTG and ATL (Author response table 1), consistently demonstrate the methodological rigor and precision of double-pulse TMS in disentangling the neural dynamics of different regions within these short temporal windows.

Author response table 1.

Double-pulse TMS studies on brain regions over 3-60 ms time interval

Response to Reviewer #1:

(1) For concern on the difficulty of disentangling the contributions of tightly-coupled brain regions to the speech-gesture integration process:

We trust that the explanation provided above has clarified this issue.

(2) For concern on the rationale for delivering HD-tDCS/TMS in set time windows for each region, as well as how these time windows were determined and how the current results compare to our previous studies from 2018 and 2023:

The current study builds on a series of investigations that systematically examined the temporal and spatial dynamics of gesture-speech integration. In our earlier work (Zhao et al., 2018, J. Neurosci), we demonstrated that interrupting neural activity in the IFG or pMTG using TMS selectively disrupted the semantic congruency effect (reaction time costs due to semantic incongruence), without affecting the gender congruency effect (reaction time costs due to gender incongruence). These findings identified the IFG and pMTG as critical hubs for gesture-speech integration. This informed the brain regions selected for subsequent studies.

In Zhao et al. (2021, J. Neurosci), we employed a double-pulse TMS protocol, delivering stimulation within one of eight 40-ms time windows, to further examine the temporal involvement of the IFG and pMTG. The results revealed time-window-selective disruptions of the semantic congruency effect, confirming the dynamic and temporally staged roles of these regions during gesture-speech integration.

In Zhao et al. (2023, Frontiers in Psychology), we investigated the semantic predictive role of gestures relative to speech by comparing two experimental conditions: (1) gestures preceding speech by a fixed interval of 200 ms, and (2) gestures preceding speech at its semantic identification point. We observed time-window-selective disruptions of the semantic congruency effect in the IFG and pMTG only in the second condition, leading to the conclusion that gestures exert a semantic priming effect on co-occurring speech. These findings underscored the semantic advantage of gesture in facilitating speech integration, further refining our understanding of the temporal and functional interplay between these modalities.

The design of the current study—including the choice of brain regions and time windows—was directly informed by these prior findings. Experiment 1 (HD-tDCS) targeted the entire gesture-speech integration process in the IFG and pMTG to assess whether neural activity in these regions, previously identified as integration hubs, is modulated by changes in informativeness from both modalities (i.e., entropy) and their interactions (mutual information, MI). The results revealed a gradual inhibition of neural activity in both areas as MI increased, evidenced by a negative correlation between MI and the tDCS inhibition effect in both regions. Building on this, Experiments 2 and 3 employed double-pulse TMS and event-related potentials (ERPs) to further assess whether the engaged neural activity was both time-sensitive and staged. These experiments also evaluated the contributions of various sources of information, revealing correlations between information-theoretic metrics and time-locked brain activity, providing insights into the ‘gradual’ nature of gesture-speech integration.

We acknowledge that the rationale for the design of the current study was not fully articulated in the original manuscript. In the revised version, we will provide a more comprehensive and coherent explanation of the logic behind the three experiments, ensuring clear alignment with our previous findings.

(3) For concern about the use of Pearson correlation and the normality of EEG data.

We appreciate the reviewer’s thoughtful consideration. In Figure 5 of the manuscript, we have already included normal distribution curves that illustrate the relationships between the average ERP amplitudes within each ROI or elicited clusters and the three information models. Additionally, multiple comparisons were addressed using FDR correction, as outlined in the manuscript.

To further clarify the data, we will calculate the Shapiro-Wilk test, a widely accepted method for assessing bivariate normality, for both the MI/entropy and averaged ERP data. The corresponding p-values will be provided in the following-up point-to-point responses.

(4) For concern about the ROI selection, and the suggestion of using whole-brain electrodes to build models of different variables (MI/entropy) to predict neural responses:

For the EEG data, we conducted both a traditional region-of-interest (ROI) analysis, with ROIs defined based on a well-established work (Habets et al., 2011), and a cluster-based permutation approach, which utilizes data-driven permutations to enhance robustness and address multiple comparisons. The latter method complements the hypothesis-driven ROI analysis by offering an exploratory, unbiased perspective. Notably, the results from both approaches were consistent, reinforcing the reliability of our findings.

To make the methods more accessible to a broader audience, we will provide a clear description of the methods used and how they relate to each other in the revised manuscript.

Reference:

Habets, B., Kita, S., Shao, Z.S., Ozyurek, A., and Hagoort, P. (2011). The Role of Synchrony and Ambiguity in Speech-Gesture Integration during Comprehension. J Cognitive Neurosci 23, 1845-1854. 10.1162/jocn.2010.21462

(5) For concern about the median split of the data:

To identify ERP components or spatiotemporal clusters that demonstrated significant semantic differences, we split each model into higher and lower halves, focusing on indexing information changes reflected by entropy or mutual information (MI). To illustrate the gradual activation process, the identified components and clusters were further analyzed for correlations with each information matrix. Remarkably, consistent results were observed between the ERP components and clusters, providing robust evidence that semantic information conveyed through gestures and speech significantly influenced the amplitude of these components or clusters. Moreover, the semantic information was shown to be highly sensitive, varying in tandem with these amplitude changes.

We acknowledge that the rationale behind this approach may not have been sufficiently clear in the initial manuscript. In our revision, we will ensure a more detailed and precise explanation to enhance the clarity and coherence of this logical framework.

Response to Reviewer #2:

We greatly appreciate Reviewer2 ’s concern regarding whether "mutual information" adequately captures the interplay between the meanings of speech and gesture. We would like to clarify that the materials used in the present study involved gestures performed without actual objects, paired with verbs that precisely describe the corresponding actions. For example, a hammering gesture was paired with the verb “hammer”, and a cutting gesture was paired with the verb “cut”. In this design, all gestures conveyed redundant meaning relative to the co-occurring speech, creating significant overlap between the information derived from speech alone and that from gesture alone.

We understand the reviewer’s concern about cases where gestures and speech may provide complementary rather than redundant information. To address this, we have developed an alternative metric for quantifying information gains contributed by supplementary multisensory cues, which will be explored in a subsequent study. However, for the present study, we believe that the observed overlap in information serves as an indicator of the degree of multisensory convergence, a central focus of our investigation.

Regarding the reviewer’s concern about how the neural processes of speech-gesture integration may change with variations in the relative timing between speech and gesture stimuli, we would like to highlight findings from our previous study (Zhao, 2023, Frontiers in Psychology). In that study, we explored the semantic predictive role of gestures relative to speech under two conditions: (1) gestures preceding speech by a fixed interval of 200 ms, and (2) gestures preceding speech of its semantic identification point. Interestingly, only in the second condition did we observe time-window-selective disruptions of the semantic congruency effect in the IFG and pMTG. This led us to conclude that gestures play a semantic priming role for co-occurring speech. Building on this, we designed the present study with gestures preceding speech of its semantic identification point to reflect this semantic priming relationship. Additionally, ongoing research is exploring gesture and speech interactions in natural conversational settings to investigate whether the neural processes identified here are consistent across varying contexts.

To prevent any similar concerns from causing doubt among the audience and to ensure clarity regarding the follow-up study, we will provide a detailed discussion of the two issues in the revised manuscript.

Response to Reviewer #3:

The primary aim of this study is to investigate whether the degree of activity in the established integration hubs, IFG and pMTG, is influenced by the information provided by gesture-speech modalities and/or their interactions. While we provided evidence for the differential involvement of the IFG and pMTG by delineating their dynamic engagement across distinct time windows of gesture-speech integration and associating these patterns with unisensory information and their interaction, we acknowledge that the mechanisms underlying these dynamics remain open to interpretation. Specifically, whether the observed effects stem from difficulties in semantic control processes, as suggested by Reviewer 3, or from resolving information uncertainty, as quantified by entropy, falls outside the scope of the current study. Importantly, we view these two interpretations as complementary rather than mutually exclusive, as both may be contributing factors. Nonetheless, we agree that addressing this question is a compelling avenue for future research. In the revised manuscript, we will include an exploratory analysis to investigate whether the confounding difficulty, stemming from the number of lexical or semantic representations, is limited to high-entropy items. Additionally, we will address and discuss alternative interpretations.

Regarding the concern of conceptual equivocation, we would like to emphasize that this study represents the first attempt to focus on the relationship between information quantity and neural engagement. In our initial presentation, we inadvertently conflated the commonly used term "graded hub," which refers to anatomical distribution, with its usage in the present context. We sincerely apologize for this oversight and are grateful for the reviewer’s careful critique. In the revised manuscript, we will clearly articulate the study’s objectives, clarify the representations of entropy and mutual information, and accurately describe their association with neural engagement.

Reference

Teige, C., Mollo, G., Millman, R., Savill, N., Smallwood, J., Cornelissen, P. L., & Jefferies, E. (2018). Dynamic semantic cognition: Characterising coherent and controlled conceptual retrieval through time using magnetoencephalography and chronometric transcranial magnetic stimulation. Cortex, 103, 329-349.

Amemiya, T., Beck, B., Walsh, V., Gomi, H., & Haggard, P. (2017). Visual area V5/hMT+ contributes to perception of tactile motion direction: a TMS study. Scientific reports, 7(1), 40937.

Muessgens, D., Thirugnanasambandam, N., Shitara, H., Popa, T., & Hallett, M. (2016). Dissociable roles of preSMA in motor sequence chunking and hand switching—a TMS study. Journal of Neurophysiology, 116(6), 2637-2646.

Vernet, M., Brem, A. K., Farzan, F., & Pascual-Leone, A. (2015). Synchronous and opposite roles of the parietal and prefrontal cortices in bistable perception: a double-coil TMS–EEG study. Cortex, 64, 78-88.

Pitcher, D. (2014). Facial expression recognition takes longer in the posterior superior temporal sulcus than in the occipital face area. Journal of Neuroscience, 34(27), 9173-9177.

Bardi, L., Kanai, R., Mapelli, D., & Walsh, V. (2012). TMS of the FEF interferes with spatial conflict. Journal of cognitive neuroscience, 24(6), 1305-1313.

D’Ausilio, A., Bufalari, I., Salmas, P., & Fadiga, L. (2012). The role of the motor system in discriminating normal and degraded speech sounds. Cortex, 48(7), 882-887.

Pitcher, D., Duchaine, B., Walsh, V., & Kanwisher, N. (2010). TMS evidence for feedforward and feedback mechanisms of face and body perception. Journal of Vision, 10(7), 671-671.

Gagnon, G., Blanchet, S., Grondin, S., & Schneider, C. (2010). Paired-pulse transcranial magnetic stimulation over the dorsolateral prefrontal cortex interferes with episodic encoding and retrieval for both verbal and non-verbal materials. Brain Research, 1344, 148-158.

Kalla, R., Muggleton, N. G., Juan, C. H., Cowey, A., & Walsh, V. (2008). The timing of the involvement of the frontal eye fields and posterior parietal cortex in visual search. Neuroreport, 19(10), 1067-1071.

Pitcher, D., Garrido, L., Walsh, V., & Duchaine, B. C. (2008). Transcranial magnetic stimulation disrupts the perception and embodiment of facial expressions. Journal of Neuroscience, 28(36), 8929-8933.

Author Response

We thank the reviewers and editorial team for the positive reaction to our paper and for the constructive recommendations and comments on our work. Here we provide a brief provisional response to key points that were identified. We will give a detailed point-by-point response with highlighted changes in our manuscript when we upload the revised version of our paper.

Reviewer 1:

Statistical evaluation of the null

In Experiment 2, we inferred the existence of a null effect of image category on suppression depth based on frequentist statistics. At the reviewer’s suggestion we performed a statistical evaluation of the evidence in favour of the null effect using a Bayesian repeated measures ANOVA implemented in JASP. That analysis provides strong evidence for the null (BF01= 20.38) and will be included in the final version of the paper.

Likelihood of exceptional cases

We acknowledge that our selection of categories is only a sampling of possible categories to which our novel tCFS method can be applied for deriving suppression depth. Other possibilities that come to mind include objects that emerge from specific configurations of simple 'tokens' such as dots (such as actions defined by biological motion (Watson et al., 2004)) or different shaped tokens configured to generate pareidolia faces (Zhou et al., 2021). We will expand on the possibility of these exceptional cases impacting bCFS and reCFS thresholds in the discussion of our revised manuscript.

Reviewer 2:

In response to the claim “the paper overreaches by claiming breakthrough thresholds are insufficient for drawing certain conclusions about subconscious processing.”

We agree that breakthrough thresholds can provide useful information to draw conclusions about unconscious processing – as our procedure is predicated on breakthrough thresholds. Our key point is that breakthrough provides only half of the needed information and will amend our manuscript accordingly. In so doing, we will also shift our focus toward the influence of semantics and low-level factors, including discussion of the possibility that suppression depth and bCFS thresholds could be driven by statistically orthogonal factors.

Reviewer 3:

On the appropriateness of log-transformed contrast

Our motivation to quantify suppression depth after log-transform to decibel scale was two-fold. First, we recognised that the traditional use of a linear contrast ramp in bCFS is at odds with the well-characterised profile of contrast discrimination thresholds which obey a power law (Legge, 1981) and the observations that neural contrast response functions show the same compressive non-linearity in many different cortical processing areas (e.g.: V1, V2, V3, V4, MT, MST, FST, TEO. See Ekstrom et al., 2009). Increasing contrast in linear steps could thus lead to a rapid saturation of the response function, which may account for the overshoot that has been reported in many canonical bCFS studies. For example, in Jiang et al. (2007), target contrast reached 100% after 1 second, yet average suppression times for faces and inverted faces were 1.36 and 1.76 seconds respectively. As contrast response functions in visual neurons saturate at high contrast, the upper levels of a linear contrast ramp have less and less effect on the target's strength. This approach to response asymptote may have exaggerated small differences between stimulus conditions and may have inflated some previously reported differences. In sum, the use of a log-transformed contrast ramp allows finer increments in contrast to be explored before saturation, a simple manipulation which we hope will be adopted by our field.

Second, by quantifying suppression depth as a decibel change, we enable the comparison of suppression depth between experiments and laboratories, which inevitably differ in presentation environments. As a comparison, a reaction-time for bCFS of 1.36 s cannot easily be compared without access to near-identical stimulation and testing environments. In addition, once ramp contrast is log-transformed it effectively linearises the neural contrast response function. This means that different studies that use different contrast levels for masker or target can be directly compared because a given suppression depth (for example, 15 dB) is the same proportionate difference between bCFS and reCFS regardless of the contrasts used in the particular study.

We also acknowledge that different stimulus categories may engage neural and visual processing associated with different contrast gain values (e.g., magno- vs parvo-mediated processing). But the breaks and returns to suppression of a given stimulus category would be dependent on the same contrast gain function appropriate for that stimulus which thus permits their direct comparison. Indeed, this is why our novel approach offers a promising technique for comparing suppression depth associated with various stimulus categories (a point mentioned above). Viewed in this way, differences in actual durations of break times (such as we report in our paper) may tell us more about differences in gain control within neural mechanisms responsible for processing of those categories.

Consider that preferential processing could shift both bCFS and reCFS thresholds together

This is related to the point raised in the previous comment. A stimulus that is preferentially processed (such as a face) could have lower bCFS and reCFS thresholds than other stimuli such that it emerges into awareness at a lower contrast but also remains visible at lower contrasts. We plan to address this interpretation of our data in our revised discussion and highlight that this type of preferential processing could well occur, and yet could still produce the same uniform suppression depth.

Can the effect of contrast ramp be explained by slower RTs?

A 500 ms reaction time estimate would not account for the magnitude of the changes observed in Experiment 3. Suppression depths in our slow, medium, and fast contrast ramps were 9.64 dB, 14.64 dB and 18.97 dB, respectively (produced by step sizes of .035, .07 and .105 dB per video frame at 60 fps). At each rate, assuming a 500 ms reaction time for both thresholds (1 second total) would capture a change of 2.1 dB, 4.2 dB, 6.3 dB. This difference cannot account for the size of the effects observed between our different ramp speeds.

Non-zero switch rate probability affecting ramping

We agree that for a given ramp speed there is a variable probability of a switch in perceptual state for both bCFS and reCFS portions of the trial. To put it in other words, for a given ramp speed and a given observer the distribution of durations at which transitions occur will exhibit variance. We see that variance in our data (just as it’s present in conventional binocular rivalry duration histograms), as a non-zero probability of switches at very short durations (for example). One might surmise that slower ramp speeds would afford more opportunity for stochastic transitions to occur and that the measured suppression depths for slow ramps are underestimates of the suppression depth produced by contrast adaptation. Yet by the same token, the same underestimation would occur during fast ramp speeds, indicating that that difference may be even larger than we reported. In our revision we will spell this out in more detail, and indicate that a non-zero probability of switches at any time may lead to an underestimation of all recorded suppression depths.

In our data, we believe the contribution of these stochastic switches are minimal. Our current Supplementary Figure 1(d) indicates that there is a non-zero probability of responses early in each ramp (e.g. durations < 2 seconds), yet these are a small proportion of all percept durations. This small proportion is clear in the empirical cumulative density function of percept durations, which we include in Author response image 1, and will address in our detailed response. Notably, during slow-ramp conditions, average percept durations actually increased, implying a resistance to any effect of early stochastic switching. We plan to expand on our analysis of these reaction-time differences in our revised manuscript.

Author response image 1.

The specificity of the DHO fit

In our revised manuscript we will increase the justification for this model, and plan to include a comparison of model fits over time (as opposed to response number in the current manuscript).

References

Ekstrom, L. B., Roelfsema, P. R., Arsenault, J. T., Kolster, H., & Vanduffel, W. (2009). Modulation of the contrast response function by electrical microstimulation of the macaque frontal eye field. The Journal of Neuroscience: The Official Journal of the Society for Neuroscience, 29(34), 10683–10694.

Jiang, Y., Costello, P., & He, S. (2007). Processing of invisible stimuli: advantage of upright faces and recognizable words in overcoming interocular suppression. Psychological Science, 18(4), 349–355.

Legge, G. E. (1981). A power law for contrast discrimination. Vision Research, 21(4), 457–467.

Watson, T. L., Pearson, J., & Clifford, C. W. G. (2004). Perceptual grouping of biological motion promotes binocular rivalry. Current Biology: CB, 14(18), 1670–1674.

Zhou, L.-F., Wang, K., He, L., & Meng, M. (2021). Twofold advantages of face processing with or without visual awareness. Journal of Experimental Psychology. Human Perception and Performance, 47(6), 784–794.

Author Response

We thank the reviewers for their useful and constructive comments. In this provisional response, we will address a few of the major issues and plan to submit a detailed, point-by-point response along with the revised manuscript.

1. Robustness of activated combination of neurons (the ‘activated ensemble’).

The reviewers have asked for additional analyses and visualization of the group of neurons activated and a classification analysis to illustrate the point that the activated set of neurons would allow discrimination between different concentrations even after the spiking activity reduced significantly in the later trials. We relied on visualization using PCA (Manuscript Fig. 4) and quantification using correlation analysis (Manuscript Fig. 5a and Manuscript Supplementary Figure 2). But this point can be easily amplified further to support our conclusions and address a major concern raised by the reviewers.

Visualization of neural responses across trials and odorants: As recommended, we followed the procedures used in Stopfer et al., 2003 (Fig. 6c) and Miura et al., 2012(Fig. 3C) to image neural responses across recorded PNs as a matrix (Author response image 1).

Author response image 1.

Author response image 1: Spike counts averaged over the entire 4s odor presentation window across all recorded neurons are shown as a function of trial number (columns). The sorting is same across different panels. Note that there are 80 neurons whose response was monitored for hexanol and octanol responses (Dataset 1; first row of panels), and 81 neurons whose response was monitored for isoamyl acetate and benzaldehyde (Dataset 2; second row of panels). As can be noted, across the 25 trials the pattern of activation remains consistent. Also, the activated combination of neurons varied robustly with odor identity and intensity.

Classification analysis: To illustrate that there is enough information to recognize an odorant and discriminate between different intensities, we performed a leave-one-trial-out classification analysis. The left-out trial was assigned the class label of its nearest neighbor (using correlation distance metric). The results from this classification analysis are shown below in Author response image 2. As a control, we shuffled the odor class labels and repeated the leave-one-trial-out classification analysis.

Author response image 2.

Author response image 2: Results from classification analysis are shown for the two datasets: hexanol–octanol at different concentrations (dataset 1; 80 PNs), and isoamyl acetate and benzaldehyde (dataset 2; 81 PNs). We did a leave-onetrial-out validation. The true odor label is shown along the x-axis and the predicted odor label is shown along the yaxis. As can be noted, the class labels for every single trial were correctly predicted in both datasets. The result after class labels were shuffled is also shown for comparison. These results strongly support our conclusion that odor intensity information is preserved and odor concentration can be recognized independent of adaptation.

Correlation with the first trial:

We had shown the correlation across odorants and concentrations as a function of the trial (manuscript Figure 5A). To complement these analyses, here we focus on the correlations with the response evoked in the first trial of each odorant at high and low concentrations and plot this information as a function of trial number (Author response image 3, 4). As can be noted, the correlation across different trials of a given odorant at specific concentrations remains much higher than all other conditions.

Author response image 3.

Author response image 3: (top-left) Correlation between 80-dimensional neural responses (averaged over the entire 4s odor presentation window) with the first trial of hexanol at high intensity (hex-H; 1% v/v) is plotted as a function of trial number. (top-right) similar plots but correlation computed with neural responses evoked during the first trial of octanol at high intensity (oct-H; 1% v/v). (bottom-left) similar plots but correlation computed with neural responses evoked in the first trial of hexanol at low intensity (hex-L; 1% v/v). (bottom-right) similar plots but correlation computed with neural responses evoked in the first trial of octanol at low intensity (oct-L; 1% v/v).

Author response image 4.

Author response image 4: (top-left) Correlation between 81-dimensional neural responses (averaged over the entire 4s odor presentation window) with the first trial of isoamyl acetate at high intensity (iaa-H; 1% v/v) is plotted as a function of trial number. (top-right) similar plots but correlation computed with neural responses evoked in the first trial of benzaldehyde at a high intensity (bza-H; 1% v/v). (bottom-left) similar plots but correlation computed with neural responses evoked in the first trial of isoamyl acetate at low intensity (iaa-L; 1% v/v). (bottom-right) similar plots but correlation computed with neural responses evoked in the first trial of benzaldehyde at low intensity (bza-L; 1% v/v).

Behavioral significance and dynamics: The reviewers had wondered about the relevance of the behavior to the organism. The maxillary palps are sensory organs close to the mouth parts that are used to grab food and help with the feeding process. In our previous studies, we had shown that these palpopening responses are innately triggered by many ‘appetitive odorants.’ However, the probability of palp opening varied across different odorants (Chandak and Raman, 2023). Some odorants evoked higher palp-opening responses and others reduced the probability of palp-opening response (below the median value across odorants). Since all other parameters (such as the clicking sound of valves, and mechanical cues due to airflow during odor presentation), are the same across these different odorants, these observed differences in palp-opening response probability are attributed to the identity of the odorants presented.

Author response image 5.

Author response image 5: Preference indices were calculated for all odors tested and are shown as a bar plot (n = 26 locusts). Blue bars indicate odors classified as appetitive, gray bars indicate neutral odors and red bars indicate unappetitive odors. Locusts with a significant deviation from the median response (one-sided binomial test, P < 0.1, were classified as either being appetitive or unappetitive; P < 0.1, P < 0.05, **P < 0.01). Error bars indicate s.e.m. [Replotted Fig 1.c from Chandak and Raman, 2023].

We had also shown that we could train locusts to have stereo-typed palp-opening responses using the classical conditioning approach (odor – odor-conditioned stimulus and food reward – unconditioned stimulus; Video: https://static- content.springer.com/esm/art%3A10.1038%2Fncomms7953/MediaObjects/41467_2015_BFncomms7953 _MOESM483_ESM.mov; Saha et al., 2015). The dynamics of those conditioned palp-opening responses have been well characterized.

We will use similar tracking procedures to monitor and quantify the dynamics of innate palp-opening responses as well. We will add supplementary videos to fully capture this behavior.

Early vs. late neural responses:

Since behavioral responses are more likely to start as soon as the odorant is presented, the reviewers wondered whether there are differences in the observed findings if we focus only on the early neural activity (as it might be more important to triggering behavior). Note that the median response time for conditioned palp-opening responses is less than 750 ms (Saha et al., 2015, Chandak and Raman, 2023). Hence, we divided the neural dataset and analyzed the neural response patterns during these early (0-750 ms after onset) and late (2-4 s after odor onset) time windows. In both these epochs, we found that the total spike counts across neurons reduced as a function of trial number or repetition and the combination of neuron activated remained robust (Author response images 6-11). Hence, we conclude that while the neural responses in different time windows would be important for shaping other parameters of behavioral response dynamics, the overall behavioral response probability that we used in our analysis had a similar relationship with early, late, or total neural activity during the entire odor presentation (i.e. time-window of the neural response did not matter for the analyses presented in the manuscript).

Author response image 6.

Author response image 6: Total spike counts reduced as a function of trial number. This reduction was observed for the total spike counts during the entire odor presentation window and during both the early (0-750 ms) and late (2-4 s) response time windows. Dataset 1: 80 PNs, hexanol, and octanol odorants.

Author response image 7.

Author response image 7: Total spike counts reduced as a function of trial number. This reduction was observed for the total spike counts during the entire odor presentation window and during both the early (0-750 ms) and late (2-4 s) response time windows. Dataset 2: 81 PNs, isoamyl acetate, and benzaldehyde odorants.

Author response image 8.

Author response image 8: Similar plots as in Figures 3 and 4 but analyzing 80-dimensional spike count vectors calculated using only the first 750 ms of odor-evoked response. Note that the correlation with the odor evoked response in the first trial remains high across trials. But between different odorants or different intensities of the same odorant, the response correlation drops significantly. Dataset 1: 80 PNs, hexanol, and octanol odorants.

Author response image 9.

Author response image 9: Similar plots as in Figures 3 and 4 but analyzing 80-dimensional spike count vectors calculated using only the last 2 seconds of odor-evoked response. Note that the correlation with the odor evoked response in the first trial remains high across trials. But between different odorants or different intensities of the same odorant, the response correlation drops significantly. Dataset 1: 80 PNs, hexanol, and octanol odorants.

Author response image 10.

Author response image 10: Similar plots as in Figures 3 and 4 but analyzing 80-dimensional spike count vectors calculated using only the first 750 ms of odor-evoked response. Note that the correlation with the odor evoked response in the first trial remains high across trials. But between different odorants or different intensities of the same odorant, the response correlation drops significantly. Dataset 2: 81 PNs, isoamyl acetate, and benzaldehyde odorants.

Author response image 11.

Author response image 11: Similar plots as in Figures 3 and 4 but analyzing 80-dimensional spike count vectors calculated using only the last 2 seconds of odor-evoked response. Note that the correlation with the odor evoked response in the first trial remains high across trials. But between different odorants or different intensities of the same odorant, the response correlation drops significantly. Dataset 2: 81 PNs, isoamyl acetate, and benzaldehyde odorants.

Other Statistical Tests:

The reviewers felt that in many analyses, we did not include error bars to indicate the sample size, SEM, or SD. We will fix this by adding the sample size information to each panel and as appropriate. However, we would also like to point out that many of the analyses are done in a trial-by-trial fashion (e.g. Manuscript Figures 3 – 6). For these analyses, it would not be possible to add SEM or SD. One condition (hex -H or iaa-H) was repeated in each dataset, and we have added them in the results shown in this response letter to demonstrate repeatability. We will strive our best to add these statistics as would be appropriate, but this cannot be done for the trial-by-trial analyses.

References:

Stopfer M, Jayaraman V, Laurent G. Intensity versus identity coding in an olfactory system. Neuron. 2003 Sep 11;39(6):991-1004. doi: 10.1016/j.neuron.2003.08.011. PMID: 12971898.

Miura K, Mainen ZF, Uchida N. Odor representations in olfactory cortex: distributed rate coding and decorrelated population activity. Neuron. 2012 Jun 21;74(6):1087-98. doi: 10.1016/j.neuron.2012.04.021. PMID: 22726838; PMCID: PMC3383608.

Chandak, R., Raman, B. Neural manifolds for odor-driven innate and acquired appetitive preferences. Nat Commun 14, 4719 (2023). https://doi.org/10.1038/s41467-023-40443-2

Saha, D., Li, C., Peterson, S. et al. Behavioural correlates of combinatorial versus temporal features of odour codes. Nat Commun 6, 6953 (2015). https://doi.org/10.1038/ncomms7953

Author response:

Reviewer #1 (Public review):

Wang et al., recorded concurrent EEG-fMRI in 107 participants during nocturnal NREM sleep to investigate brain activity and connectivity related to slow oscillations (SO), sleep spindles, and in particular their co-occurrence. The authors found SO-spindle coupling to be correlated with increased thalamic and hippocampal activity, and with increased functional connectivity from the hippocampus to the thalamus and from the thalamus to the neocortex, especially the medial prefrontal cortex (mPFC). They concluded the brain-wide activation pattern to resemble episodic memory processing, but to be dissociated from task-related processing and suggest that the thalamus plays a crucial role in coordinating the hippocampal-cortical dialogue during sleep.

The paper offers an impressively large and highly valuable dataset that provides the opportunity for gaining important new insights into the network substrate involved in SOs, spindles, and their coupling. However, the paper does unfortunately not exploit the full potential of this dataset with the analyses currently provided, and the interpretation of the results is often not backed up by the results presented. I have the following specific comments.

Thank you for your thoughtful and constructive feedback. We greatly appreciate your recognition of the strengths of our dataset and findings Below, we address your specific comments and provide responses to each point you raised to ensure our methods and results are as transparent and comprehensible as possible. We hope these revisions address your comments and further strengthen our manuscript. Thank you again for the constructive feedback.

(1) The introduction is lacking sufficient review of the already existing literature on EEG-fMRI during sleep and the BOLD-correlates of slow oscillations and spindles in particular (Laufs et al., 2007; Schabus et al., 2007; Horovitz et al., 2008; Laufs, 2008; Czisch et al., 2009; Picchioni et al., 2010; Spoormaker et al., 2010; Caporro et al., 2011; Bergmann et al., 2012; Hale et al., 2016; Fogel et al., 2017; Moehlman et al., 2018; Ilhan-Bayrakci et al., 2022). The few studies mentioned are not discussed in terms of the methods used or insights gained.

We acknowledge the need for a more comprehensive review of prior EEG-fMRI studies investigating BOLD correlates of slow oscillations and spindles. However, these articles are not all related to sleep SO or spindle. Articles (Hale et al., 2016; Horovitz et al., 2008; Laufs, 2008; Laufs, Walker, & Lund, 2007; Spoormaker et al., 2010) mainly focus on methodology for EEG-fMRI, sleep stages, or brain networks, which are not the focus of our study. Thank you again for your attention to the comprehensiveness of our literature review, and we will expand the introduction to include a more detailed discussion of the existing literature, ensuring that the contributions of previous EEG-fMRI sleep studies are adequately acknowledged.

Introduction, Page 4 Lines 62-76

“Investigating these sleep-related neural processes in humans is challenging because it requires tracking transient sleep rhythms while simultaneously assessing their widespread brain activation. Recent advances in simultaneous EEG-fMRI techniques provide a unique opportunity to explore these processes. EEG allows for precise event-based detection of neural signal, while fMRI provides insight into the broader spatial patterns of brain activation and functional connectivity (Horovitz et al., 2008; Huang et al., 2024; Laufs, 2008; Laufs, Walker, & Lund, 2007; Schabus et al., 2007; Spoormaker et al., 2010). Previous EEG-fMRI studies on sleep have focused on classifying sleep stages or examining the neural correlates of specific waves (Bergmann et al., 2012; Caporro et al., 2012; Czisch et al., 2009; Fogel et al., 2017; Hale et al., 2016; Ilhan-Bayrakcı et al., 2022; Moehlman et al., 2019; Picchioni et al., 2011). These studies have generally reported that slow oscillations are associated with widespread cortical and subcortical BOLD changes, whereas spindles elicit activation in the thalamus, as well as in several cortical and paralimbic regions. Although these findings provide valuable insights into the BOLD correlates of sleep rhythms, they often do not employ sophisticated temporal modeling (Huang et al., 2024), to capture the dynamic interactions between different oscillatory events, e.g., the coupling between SOs and spindles.”

(2) The paper falls short in discussing the specific insights gained into the neurobiological substrate of the investigated slow oscillations, spindles, and their interactions. The validity of the inverse inference approach ("Open ended cognitive state decoding"), assuming certain cognitive functions to be related to these oscillations because of the brain regions/networks activated in temporal association with these events, is debatable at best. It is also unclear why eventually only episodic memory processing-like brain-wide activation is discussed further, despite the activity of 16 of 50 feature terms from the NeuroSynth v3 dataset were significant (episodic memory, declarative memory, working memory, task representation, language, learning, faces, visuospatial processing, category recognition, cognitive control, reading, cued attention, inhibition, and action).

Thank you for pointing this out, particularly regarding the use of inverse inference approaches such as “open-ended cognitive state decoding.” Given the concerns about the indirectness of this approach, we decided to remove its related content and results from Figure 3 in the main text and include it in Supplementary Figure 7. We will refocus the main text on direct neurobiological insights gained from our EEG-fMRI analyses, particularly emphasizing the hippocampal-thalamocortical network dynamics underlying SO-spindle coupling, and we will acknowledge the exploratory nature of these findings and highlight their limitations.

Discussion, Page 17-18 Lines 323-332

“To explore functional relevance, we employed an open-ended cognitive state decoding approach using meta-analytic data (NeuroSynth: Yarkoni et al. (2011)). Although this method usefully generates hypotheses about potential cognitive processes, particularly in the absence of a pre- and post-sleep memory task, it is inherently indirect. Many cognitive terms showed significant associations (16 of 50), such as “episodic memory,” “declarative memory,” and “working memory.” We focused on episodic/declarative memory given the known link with hippocampal reactivation (Diekelmann & Born, 2010; Staresina et al., 2015; Staresina et al., 2023). Nonetheless, these inferences regarding memory reactivation should be interpreted cautiously without direct behavioral measures. Future research incorporating explicit tasks before and after sleep would more rigorously validate these potential functional claims.”

(3) Hippocampal activation during SO-spindles is stated as a main hypothesis of the paper - for good reasons - however, other regions (e.g., several cortical as well as thalamic) would be equally expected given the known origin of both oscillations and the existing sleep-EEG-fMRI literature. However, this focus on the hippocampus contrasts with the focus on investigating the key role of the thalamus instead in the Results section.

We appreciate your insight regarding the relative emphasis on hippocampal and thalamic activation in our study. We recognize that the manuscript may currently present an inconsistency between our initial hypothesis and the main focus of the results. To address this concern, we will ensure that our Introduction and Discussion section explicitly discusses both regions, highlighting the complementary roles of the hippocampus (memory processing and reactivation) and the thalamus (spindle generation and cortico-hippocampal coordination) in SO-spindle dynamics.

Introduction, Page 5 Lines 87-103

“To address this gap, our study investigates brain-wide activation and functional connectivity patterns associated with SO-spindle coupling, and employs a cognitive state decoding approach (Margulies et al., 2016; Yarkoni et al., 2011)—albeit indirectly—to infer potential cognitive functions. In the current study, we used simultaneous EEG-fMRI recordings during nocturnal naps (detailed sleep staging results are provided in the Methods and Table S1) in 107 participants. Although directly detecting hippocampal ripples using scalp EEG or fMRI is challenging, we expected that hippocampal activation in fMRI would coincide with SO-spindle coupling detected by EEG, given that SOs, spindles, and ripples frequently co-occur during NREM sleep. We also anticipated a critical role of the thalamus, particularly thalamic spindles, in coordinating hippocampal-cortical communication.

We found significant coupling between SOs and spindles during NREM sleep (N2/3), with spindle peaks occurring slightly before the SO peak. This coupling was associated with increased activation in both the thalamus and hippocampus, with functional connectivity patterns suggesting thalamic coordination of hippocampal-cortical communication. These findings highlight the key role of the thalamus in coordinating hippocampal-cortical interactions during human sleep and provide new insights into the neural mechanisms underlying sleep-dependent brain communication. A deeper understanding of these mechanisms may contribute to future neuromodulation approaches aimed at enhancing sleep-dependent cognitive function and treating sleep-related disorders.”

Discussion, Page 16-17 Lines 292-307

“When modeling the timing of these sleep rhythms in the fMRI, we observed hippocampal activation selectively during SO-spindle events. This suggests the possibility of triple coupling (SOs–spindles–ripples), even though our scalp EEG was not sufficiently sensitive to detect hippocampal ripples—key markers of memory replay (Buzsáki, 2015). Recent iEEG evidence indicates that ripples often co-occur with both spindles (Ngo, Fell, & Staresina, 2020) and SOs (Staresina et al., 2015; Staresina et al., 2023). Therefore, the hippocampal involvement during SO-spindle events in our study may reflect memory replay from the hippocampus, propagated via thalamic spindles to distributed cortical regions.

The thalamus, known to generate spindles (Halassa et al., 2011), plays a key role in producing and coordinating sleep rhythms (Coulon, Budde, & Pape, 2012; Crunelli et al., 2018), while the hippocampus is found essential for memory consolidation (Buzsáki, 2015; Diba & Buzsá ki, 2007; Singh, Norman, & Schapiro, 2022). The increased hippocampal and thalamic activity, along with strengthened connectivity between these regions and the mPFC during SO-spindle events, underscores a hippocampal-thalamic-neocortical information flow. This aligns with recent findings suggesting the thalamus orchestrates neocortical oscillations during sleep (Schreiner et al., 2022). The thalamus and hippocampus thus appear central to memory consolidation during sleep, guiding information transfer to the neocortex, e.g., mPFC.”

(4) The study included an impressive number of 107 subjects. It is surprising though that only 31 subjects had to be excluded under these difficult recording conditions, especially since no adaptation night was performed. Since only subjects were excluded who slept less than 10 min (or had excessive head movements) there are likely several datasets included with comparably short durations and only a small number of SOs and spindles and even less combined SO-spindle events. A comprehensive table should be provided (supplement) including for each subject (included and excluded) the duration of included NREM sleep, number of SOs, spindles, and SO+spindle events. Also, some descriptive statistics (mean/SD/range) would be helpful.

We appreciate your recognition of our sample size and the challenges associated with simultaneous EEG-fMRI sleep recordings. We acknowledge the importance of transparently reporting individual subject data, particularly regarding sleep duration and the number of detected SOs, spindles, and SO-spindle events. To address this, we will provide comprehensive tables in the supplementary materials, contains descriptive information about sleep-related characteristics (Table S1), as well as detailed information about sleep waves at each sleep stage for all 107 subjects(Table S2-S4), listing for each subject:(1)Different sleep stage duration; (2)Number of detected SOs; (3)Number of detected spindles; (4)Number of detected SO-spindle coupling events; (5)Density of detected SOs; (6)Density of detected spindles; (7)Density of detected SO-spindle coupling events.

However, most of the excluded participants were unable to fall asleep or had too short a sleep duration, so they basically had no NREM sleep period, so it was impossible to count the NREM sleep duration, SO, spindle, and coupling numbers.

Supplementary Materials, Page 42-54, Table S1-S4

(Consider of the length, we do not list all the tables here. Please refer to the revised manuscript.)

(5) Was the 20-channel head coil dedicated for EEG-fMRI measurements? How were the electrode cables guided through/out of the head coil? Usually, the 64-channel head coil is used for EEG-fMRI measurements in a Siemens PRISMA 3T scanner, which has a cable duct at the back that allows to guide the cables straight out of the head coil (to minimize MR-related artifacts). The choice for the 20-channel head coil should be motivated. Photos of the recording setup would also be helpful.

Thank you for your comment regarding our choice of the 20-channel head coil for EEG-fMRI measurements. We acknowledge that the 64-channel head coil is commonly used in Siemens PRISMA 3T scanners; however, the 20-channel coil was selected due to specific practical and technical considerations in our study. In particular, the 20-channel head coil was compatible with our EEG system and ensured sufficient signal-to-noise ratio (SNR) for both EEG and fMRI acquisition. The EEG electrode cables were guided through the lateral and posterior openings of the head coil, secured with foam padding to reduce motion and minimize MR-related artifacts. Moreover, given the extended nature of nocturnal sleep recordings, the 20-channel coil allowed us to maintain participant comfort while still achieving high-quality simultaneous EEG-fMRI data.

We have made this clearer in the revised manuscript.

Methods, Page 20 Lines 385-392

“All MRI data were acquired using a 20-channel head coil on a research-dedicated 3-Tesla Siemens Magnetom Prisma MRI scanner. Earplugs and cushions were provided for noise protection and head motion restriction. We chose the 20-channel head coil because it was compatible with our EEG system and ensured sufficient signal-to-noise ratio (SNR) for both EEG and fMRI acquisition. The EEG electrode cables were guided through the lateral and posterior openings of the head coil, secured with foam padding to reduce motion and minimize MR-related artifacts. Moreover, given the extended nature of nocturnal sleep recordings, the 20-channel coil helped maintain participant comfort while still achieving high-quality simultaneous EEG-fMRI data.”

(6) Was the EEG sampling synchronized to the MR scanner (gradient system) clock (the 10 MHz signal; not referring to the volume TTL triggers here)? This is a requirement for stable gradient artifact shape over time and thus accurate gradient noise removal.

Thank you for raising this important point. We confirm that the EEG sampling was synchronized to the MR scanner’s 10 MHz gradient system clock, ensuring a stable gradient artifact shape over time and enabling accurate artifact removal. This synchronization was achieved using the standard clock synchronization interface of the EEG amplifier, minimizing timing jitter and drift. As a result, the gradient artifact waveform remained stable across volumes, allowing for more effective artifact correction during preprocessing. We appreciate your attention to this critical aspect of EEG-fMRI data acquisition.

We have made this clearer in the revised manuscript.

Methods, Page 19-20 Lines 371-383

“EEG was recorded simultaneously with fMRI data using an MR-compatible EEG amplifier system (BrainAmps MR-Plus, Brain Products, Germany), along with a specialized electrode cap. The recording was done using 64 channels in the international 10/20 system, with the reference channel positioned at FCz. In order to adhere to polysomnography (PSG) recording standards, six electrodes were removed from the EEG cap: one for electrocardiogram (ECG) recording, two for electrooculogram (EOG) recording, and three for electromyogram (EMG) recording. EEG data was recorded at a sample rate of 5000 Hz, the resistance of the reference and ground channels was kept below 10 kΩ, and the resistance of the other channels was kept below 20 kΩ. To synchronize the EEG and fMRI recordings, the BrainVision recording software (BrainProducts, Germany) was utilized to capture triggers from the MRI scanner. The EEG sampling was synchronized to the MR scanner’s 10 MHz gradient system clock, ensuring a stable gradient artifact shape over time and enabling accurate artifact removal. This was achieved via the standard clock synchronization interface of the EEG amplifier, minimizing timing jitter and drift.”

(7) The TR is quite long and the voxel size is quite large in comparison to state-of-the-art EPI sequences. What was the rationale behind choosing a sequence with relatively low temporal and spatial resolution?

We acknowledge that our chosen TR and voxel size are relatively long and large compared to state-of-the-art EPI sequences. This decision was made to optimize the signal-to-noise ratio (SNR) and reduce susceptibility-related distortions, which are particularly critical in EEG-fMRI sleep studies where head motion and physiological noise can be substantial. A longer TR allowed us to sample whole-brain activity with sufficient coverage, while a larger voxel size helped enhance BOLD sensitivity and minimize partial volume effects in deep brain structures such as the thalamus and hippocampus, which are key regions of interest in our study. We appreciate your concern and hope this clarification provides sufficient rationale for our sequence parameters.

We have made this clearer in the revised manuscript.

Methods, Page 20-21 Lines 398-408

“Then, the “sleep” session began after the participants were instructed to try and fall asleep. For the functional scans, whole-brain images were acquired using k-space and steady-state T2*-weighted gradient echo-planar imaging (EPI) sequence that is sensitive to the BOLD contrast. This measures local magnetic changes caused by changes in blood oxygenation that accompany neural activity (sequence specification: 33 slices in interleaved ascending order, TR = 2000 ms, TE = 30 ms, voxel size = 3.5 × 3.5 × 4.2 mm³, FA = 90°, matrix = 64 × 64, gap = 0.7 mm). A relatively long TR and larger voxel size were chosen to optimize SNR and reduce susceptibility-related distortions, which are critical in EEG-fMRI sleep studies where head motion and physiological noise can be substantial. The longer TR allowed whole-brain coverage with sufficient temporal resolution, while the larger voxel size helped enhance BOLD sensitivity and minimize partial volume effects in deep brain structures (e.g., the thalamus and hippocampus), which are key regions of interest in this study.”

(8) The anatomically defined ROIs are quite large. It should be elaborated on how this might reduce sensitivity to sleep rhythm-specific activity within sub-regions, especially for the thalamus, which has distinct nuclei involved in sleep functions.

We appreciate your insight regarding the use of anatomically defined ROIs and their potential limitations in detecting sleep rhythm-specific activity within sub-regions, particularly in the thalamus. Given the distinct functional roles of thalamic nuclei in sleep processes, we acknowledge that using a single, large thalamic ROI may reduce sensitivity to localized activity patterns. To address this, we will discuss this limitation in the revised manuscript, acknowledging that our approach prioritizes whole-structure effects but may not fully capture nucleus-specific contributions.

Discussion, Page 18 Lines 333-341

“Despite providing new insights, our study has several limitations. First, our scalp EEG did not directly capture hippocampal ripples, preventing us from conclusively demonstrating triple coupling. Second, the combination of EEG-fMRI and the lack of a memory task limit our ability to parse fine-grained BOLD responses at the DOWN- vs. UP-states of SOs and link observed activations to behavioral outcomes. Third, the use of large anatomical ROIs may mask subregional contributions of specific thalamic nuclei or hippocampal subfields. Finally, without a memory task, we cannot establish a direct behavioral link between sleep-rhythm-locked activation and memory consolidation. Future studies combining techniques such as ultra-high-field fMRI or iEEG with cognitive tasks may refine our understanding of subregional network dynamics and functional significance during sleep.”

(9) The study reports SO & spindle amplitudes & densities, as well as SO+spindle coupling, to be larger during N2/3 sleep compared to N1 and REM sleep, which is trivial but can be seen as a sanity check of the data. However, the amount of SOs and spindles reported for N1 and REM sleep is concerning, as per definition there should be hardly any (if SOs or spindles occur in N1 it becomes by definition N2, and the interval between spindles has to be considerably large in REM to still be scored as such). Thus, on the one hand, the report of these comparisons takes too much space in the main manuscript as it is trivial, but on the other hand, it raises concerns about the validity of the scoring.

We appreciate your concern regarding the reported presence of SOs and spindles in N1 and REM sleep and the potential implications. Our detection method for detecting SO, spindle, and coupling were originally designed only for N2&N3 sleep data based on the characteristics of the data itself, and this method is widely recognized and used in the sleep research (Hahn et al., 2020; Helfrich et al., 2019; Helfrich et al., 2018; Ngo, Fell, & Staresina, 2020; Schreiner et al., 2022; Schreiner et al., 2021; Staresina et al., 2015; Staresina et al., 2023). While, because the detection methods for SO and spindle are based on percentiles, this method will always detect a certain number of events when used for other stages (N1 and REM) sleep data, but the differences between these events and those detected in stage N23 remain unclear. We will acknowledge the reasons for these results in the Methods section and emphasize that they are used only for sanity checks.

Methods, Page 25 Lines 515-524

“We note that the above methods for detecting SOs, spindles, and their couplings were originally developed for N2 and N3 sleep data, based on the specific characteristics of these stages. These methods are widely recognized in sleep research (Hahn et al., 2020; Helfrich et al., 2019; Helfrich et al., 2018; Ngo, Fell, & Staresina, 2020; Schreiner et al., 2022; Schreiner et al., 2021; Staresina et al., 2015; Staresina et al., 2023). However, because this percentile-based detection approach will inherently identify a certain number of events if applied to other stages (e.g., N1 and REM), the nature of these events in those stages remains unclear compared to N2/N3. We nevertheless identified and reported the detailed descriptive statistics of these sleep rhythms in all sleep stages, under the same operational definitions, both for completeness and as a sanity check. Within the same subject, there should be more SOs, spindles, and their couplings in N2/N3 than in N1 or REM (see also Figure S2-S4, Table S1-S4).”

(10) Why was electrode F3 used to quantify the occurrence of SOs and spindles? Why not a midline frontal electrode like Fz (or a number of frontal electrodes for SOs) and Cz (or a number of centroparietal electrodes) for spindles to be closer to their maximum topography?

We appreciate your suggestion regarding electrode selection for SO and spindle quantification. Our choice of F3 was primarily based on previous studies (Massimini et al., 2004; Molle et al., 2011), where bilateral frontal electrodes are commonly used for detecting SOs and spindles. Additionally, we considered the impact of MRI-related noise and, after a comprehensive evaluation, determined that F3 provided an optimal balance between signal quality and artifact minimization. We also acknowledge that alternative electrode choices, such as Fz for SOs and Cz for spindles, could provide additional insights into their topographical distributions.

(11) Functional connectivity (hippocampus -> thalamus -> cortex (mPFC)) is reported to be increased during SO-spindle coupling and interpreted as evidence for coordination of hippocampo-neocortical communication likely by thalamic spindles. However, functional connectivity was only analysed during coupled SO+spindle events, not during isolated SOs or isolated spindles. Without the direct comparison of the connectivity patterns between these three events, it remains unclear whether this is specific for coupled SO+spindle events or rather associated with one or both of the other isolated events. The PPIs need to be conducted for those isolated events as well and compared statistically to the coupled events.

We appreciate your critical perspective on our functional connectivity analysis and the interpretation of hippocampus-thalamus-cortex (mPFC) interactions during SO-spindle coupling. We acknowledge that, in the current analysis, functional connectivity was only examined during coupled SO-spindle events, without direct comparison to isolated SOs or isolated spindles. To address this concern, we have conducted PPI analyses for all three ROIs(Hippocampus, Thalamus, mPFC) and all three event types (SO-spindle couplings, isolated SOs, and isolated spindles). Our results indicate that neither isolated SOs nor isolated Spindles yielded significant connectivity changes in all three ROIs, as all failed to survive multiple comparison corrections. This suggests that the observed connectivity increase is specific to SO-spindle coupling, rather than being independently driven by either SOs or spindles alone.

Results, Page 14 Lines 248-255

“Crucially, the interaction between FC and SO-spindle coupling revealed that only the functional connectivity of hippocampus -> thalamus (ROI analysis, t₍₁₀₆₎ = 1.86, p = 0.0328) and thalamus -> mPFC (ROI analysis, t₍₁₀₆₎ = 1.98, p = 0.0251) significantly increased during SO-spindle coupling, with no significant changes in all other pathways (Fig. 4e). We also conducted PPI analyses for the other two events (SOs and spindles), and neither yielded significant connectivity changes in the three ROIs, as all failed to survive whole-brain FWE correction at the cluster level (p < 0.05). Together, these findings suggest that the thalamus, likely via spindles, coordinates hippocampal-cortical communication selectively during SO-spindle coupling, but not isolated SOs or spindle events alone.”

(12) The limited temporal resolution of fMRI does indeed not allow for easily distinguishing between fMRI activation patterns related to SO-up- vs. SO-down-states. For this, one could try to extract the amplitudes of SO-up- and SO-down-states separately for each SO event and model them as two separate parametric modulators (with the risk of collinearity as they are likely correlated).

We appreciate your insightful comment regarding the challenge of distinguishing fMRI activation patterns related to SO-up vs. SO-down states due to the limited temporal resolution of fMRI. While our current analysis does not differentiate between these two phases, we acknowledge that separately modeling SO-up and SO-down states using parametric modulators could provide a more refined understanding of their distinct neural correlates. However, as you notes, this approach carries the risk of collinearity, and there is indeed a high correlation between the two amplitudes across all subjects in our results (r=0.98). Future studies could explore more on leveraging high-temporal-resolution techniques. While implementing this in the current study is beyond our scope, we will acknowledge this limitation in the Discussion section.

Discussion, Page 17 Lines 308-322

“An intriguing aspect of our findings is the reduced DMN activity during SOs when modeled at the SO trough (DOWN-state). This reduced DMN activity may reflect large-scale neural inhibition characteristic of the SO trough. The DMN is typically active during internally oriented cognition (e.g., self-referential processing or mind-wandering) and is suppressed during external stimuli processing (Yeshurun, Nguyen, & Hasson, 2021). It is unlikely, however, that this suppression of DMN during SO events is related to a shift from internal cognition to external responses given it is during deep sleep time. Instead, it could be driven by the inherent rhythmic pattern of SOs, which makes it difficult to separate UP- from DOWN-states (the two temporal regressors were highly correlated, and similar brain activation during SOs events was obtained if modelled at the SO peak instead, Fig. S5). Since the amplitude at the SO trough is consistently larger than that at the SO peak, the neural activation we detected may primarily capture the large-scale inhibition from DOWN-state. Interestingly, no such DMN reduction was found during SO-spindle coupling, implying that coupling may involve distinct neural dynamics that partially re-engage DMN-related processes, possibly reflecting memory-related reactivation. Future research using high-temporal-resolution techniques like iEEG could clarify these possibilities.”

Discussion, Page 18 Lines 333-341

“Despite providing new insights, our study has several limitations. First, our scalp EEG did not directly capture hippocampal ripples, preventing us from conclusively demonstrating triple coupling. Second, the combination of EEG-fMRI and the lack of a memory task limit our ability to parse fine-grained BOLD responses at the DOWN- vs. UP-states of SOs and link observed activations to behavioral outcomes. Third, the use of large anatomical ROIs may mask subregional contributions of specific thalamic nuclei or hippocampal subfields. Finally, without a memory task, we cannot establish a direct behavioral link between sleep-rhythm-locked activation and memory consolidation. Future studies combining techniques such as ultra-high-field fMRI or iEEG with cognitive tasks may refine our understanding of subregional network dynamics and functional significance during sleep.”

(13) L327: "It is likely that our findings of diminished DMN activity reflect brain activity during the SO DOWN-state, as this state consistently shows higher amplitude compared to the UP-state within subjects, which is why we modelled the SO trough as its onset in the fMRI analysis." This conclusion is not justified as the fact that SO down-states are larger in amplitude does not mean their impact on the BOLD response is larger.

We appreciate your concern regarding our interpretation of diminished DMN activity reflecting the SO down-state. We acknowledge that the current expression is somewhat misleading, and our interpretation of it is: it could be driven by the inherent rhythmic pattern of SOs, which makes it difficult to separate UP- from DOWN-states (the two temporal regressors were highly correlated, and similar brain activation during SOs events was obtained if modelled at the SO peak instead). Since the amplitude at the SO trough is consistently larger than that at the SO peak, the neural activation we detected may primarily capture the large-scale inhibition from DOWN-state. And we will make this clear in the Discussion section.

Discussion, Page 17 Lines 308-322

“An intriguing aspect of our findings is the reduced DMN activity during SOs when modeled at the SO trough (DOWN-state). This reduced DMN activity may reflect large-scale neural inhibition characteristic of the SO trough. The DMN is typically active during internally oriented cognition (e.g., self-referential processing or mind-wandering) and is suppressed during external stimuli processing (Yeshurun, Nguyen, & Hasson, 2021). It is unlikely, however, that this suppression of DMN during SO events is related to a shift from internal cognition to external responses given it is during deep sleep time. Instead, it could be driven by the inherent rhythmic pattern of SOs, which makes it difficult to separate UP- from DOWN-states (the two temporal regressors were highly correlated, and similar brain activation during SOs events was obtained if modelled at the SO peak instead, Fig. S5). Since the amplitude at the SO trough is consistently larger than that at the SO peak, the neural activation we detected may primarily capture the large-scale inhibition from DOWN-state. Interestingly, no such DMN reduction was found during SO-spindle coupling, implying that coupling may involve distinct neural dynamics that partially re-engage DMN-related processes, possibly reflecting memory-related reactivation. Future research using high-temporal-resolution techniques like iEEG could clarify these possibilities.”

(14) Line 77: "In the current study, while directly capturing hippocampal ripples with scalp EEG or fMRI is difficult, we expect to observe hippocampal activation in fMRI whenever SOs-spindles coupling is detected by EEG, if SOs- spindles-ripples triple coupling occurs during human NREM sleep". Not all SO-spindle events are associated with ripples (Staresina et al., 2015), but hippocampal activation may also be expected based on the occurrence of spindles alone (Bergmann et al., 2012).

We appreciate your clarification regarding the relationship between SO-spindle coupling and hippocampal ripples. We acknowledge that not all SO-spindle events are necessarily accompanied by ripples (Staresina et al., 2015). However, based on previous research, we found that hippocampal ripples are significantly more likely to occur during SO-spindle coupling events. This suggests that while ripple occurrence is not guaranteed, SO-spindle coupling creates a favorable network state for ripple generation and potential hippocampal activation. To ensure accuracy, we will revise the manuscript to delete this misleading sentence in the Introduction section and acknowledge in the Discussion that our results cannot conclusively directly observe the triple coupling of SO, spindle, and hippocampal ripples.

Discussion, Page 18 Lines 333-341

“Despite providing new insights, our study has several limitations. First, our scalp EEG did not directly capture hippocampal ripples, preventing us from conclusively demonstrating triple coupling. Second, the combination of EEG-fMRI and the lack of a memory task limit our ability to parse fine-grained BOLD responses at the DOWN- vs. UP-states of SOs and link observed activations to behavioral outcomes. Third, the use of large anatomical ROIs may mask subregional contributions of specific thalamic nuclei or hippocampal subfields. Finally, without a memory task, we cannot establish a direct behavioral link between sleep-rhythm-locked activation and memory consolidation. Future studies combining techniques such as ultra-high-field fMRI or iEEG with cognitive tasks may refine our understanding of subregional network dynamics and functional significance during sleep.”

Reviewer #2 (Public review):

In this study, Wang and colleagues aimed to explore brain-wide activation patterns associated with NREM sleep oscillations, including slow oscillations (SOs), spindles, and SO-spindle coupling events. Their findings reveal that SO-spindle events corresponded with increased activation in both the thalamus and hippocampus. Additionally, they observed that SO-spindle coupling was linked to heightened functional connectivity from the hippocampus to the thalamus, and from the thalamus to the medial prefrontal cortex-three key regions involved in memory consolidation and episodic memory processes.

This study's findings are timely and highly relevant to the field. The authors' extensive data collection, involving 107 participants sleeping in an fMRI while undergoing simultaneous EEG recording, deserves special recognition. If shared, this unique dataset could lead to further valuable insights. While the conclusions of the data seem overall well supported by the data, some aspects with regard to the detection of sleep oscillations need clarification.

The authors report that coupled SO-spindle events were most frequent during NREM sleep (2.46 [plus minus] 0.06 events/min), but they also observed a surprisingly high occurrence of these events during N1 and REM sleep (2.23 [plus minus] 0.09 and 2.32 [plus minus] 0.09 events/min, respectively), where SO-spindle coupling would not typically be expected. Combined with the relatively modest SO amplitudes reported (~25 µV, whereas >75 µV would be expected when using mastoids as reference electrodes), this raises the possibility that the parameters used for event detection may not have been conservative enough - or that sleep staging was inaccurately performed. This issue could present a significant challenge, as the fMRI findings are largely dependent on the reliability of these detected events.

Thank you very much for your thorough and encouraging review. We appreciate your recognition of the significance and relevance of our study and dataset, particularly in highlighting how simultaneous EEG-fMRI recordings can provide complementary insights into the temporal dynamics of neural oscillations and their associated spatial activation patterns during sleep. In the sections that follow, we address each of your comments in detail. We have revised the text and conducted additional analyses wherever possible to strengthen our argument, clarify our methodological choices. We believe these revisions improve the clarity and rigor of our work, and we thank you for helping us refine it.

We appreciate your insightful comments regarding the detection of sleep oscillations. Our methods for detecting SOs, spindles, and their couplings were originally developed for N2 and N3 sleep data, based on the specific characteristics of these stages. These methods are widely recognized in sleep research (Hahn et al., 2020; Helfrich et al., 2019; Helfrich et al., 2018; Ngo, Fell, & Staresina, 2020; Schreiner et al., 2022; Schreiner et al., 2021; Staresina et al., 2015; Staresina et al., 2023). However, because this percentile-based detection approach will inherently identify a certain number of events if applied to other stages (e.g., N1 and REM), the nature of these events in those stages remains unclear compared to N2/N3. We nevertheless identified and reported the detailed descriptive statistics of these sleep rhythms in all sleep stages, under the same operational definitions, both for completeness and as a sanity check. Within the same subject, there should be more SOs, spindles, and their couplings in N2/N3 than in N1 or REM. We will acknowledge the reasons for these results in the Methods section and emphasize that they are used only for sanity checks.

Regarding the reported SO amplitudes (~25 µV), during preprocessing, we applied the Signal Space Projection (SSP) method to more effectively remove MRI gradient artifacts and cardiac pulse noise. While this approach enhances data quality, it also reduces overall signal power, leading to systematically lower reported amplitudes. Despite this, our SO detection in NREM sleep (especially N2/N3) remain physiologically meaningful and are consistent with previous fMRI studies using similar artifact removal techniques. We appreciate your careful evaluation and valuable suggestions.

In addition, we will provide comprehensive tables in the supplementary materials, contains descriptive information about sleep-related characteristics (Table S1), as well as detailed information about sleep waves at each sleep stage for all 107 subjects(Table S2-S4), listing for each subject:(1)Different sleep stage duration; (2)Number of detected SOs; (3)Number of detected spindles; (4)Number of detected SO-spindle coupling events; (2)Density of detected SOs; (3)Density of detected spindles; (4)Density of detected SO-spindle coupling events.

Methods, Page 25 Lines 515-524

“We note that the above methods for detecting SOs, spindles, and their couplings were originally developed for N2 and N3 sleep data, based on the specific characteristics of these stages. These methods are widely recognized in sleep research (Hahn et al., 2020; Helfrich et al., 2019; Helfrich et al., 2018; Ngo, Fell, & Staresina, 2020; Schreiner et al., 2022; Schreiner et al., 2021; Staresina et al., 2015; Staresina et al., 2023). However, because this percentile-based detection approach will inherently identify a certain number of events if applied to other stages (e.g., N1 and REM), the nature of these events in those stages remains unclear compared to N2/N3. We nevertheless identified and reported the detailed descriptive statistics of these sleep rhythms in all sleep stages, under the same operational definitions, both for completeness and as a sanity check. Within the same subject, there should be more SOs, spindles, and their couplings in N2/N3 than in N1 or REM (see also Figure S2-S4, Table S1-S4).”

Supplementary Materials, Page 42-54, Table S1-S4

(Consider of the length, we do not list all the tables here. Please refer to the revised manuscript.)

Reviewer #3 (Public review):

Summary:

Wang et al., examined the brain activity patterns during sleep, especially when locked to those canonical sleep rhythms such as SO, spindle, and their coupling. Analyzing data from a large sample, the authors found significant coupling between spindles and SOs, particularly during the upstate of the SO. Moreover, the authors examined the patterns of whole-brain activity locked to these sleep rhythms. To understand the functional significance of these brain activities, the authors further conducted open-ended cognitive state decoding and found a variety of cognitive processing may be involved during SO-spindle coupling and during other sleep events. The authors next investigated the functional connectivity analyses and found enhanced connectivity between the hippocampus, the thalamus, and the medial PFC. These results reinforced the theoretical model of sleep-dependent memory consolidation, such that SO-spindle coupling is conducive to systems-level memory reactivation and consolidation.

Strengths:

There are obvious strengths in this work, including the large sample size, state-of-the-art neuroimaging and neural oscillation analyses, and the richness of results.

Weaknesses:

Despite these strengths and the insights gained, there are weaknesses in the design, the analyses, and inferences.

Thank you for your detailed and thoughtful review of our manuscript. We are delighted that you recognize our advanced analysis methods and rich results of neuroimaging and neural oscillations as well as the large sample size data. In the following sections, we provide detailed responses to each of your comments. And we have revised the text and conducted additional analyses to strengthen our arguments and clarify our methodological choices. We believe these revisions enhance the clarity and rigor of our work, and we sincerely appreciate your thoughtful feedback in helping us refine the manuscript.

(1) A repeating statement in the manuscript is that brain activity could indicate memory reactivation and thus consolidation. This is indeed a highly relevant question that could be informed by the current data/results. However, an inherent weakness of the design is that there is no memory task before and after sleep. Thus, it is difficult (if not impossible) to make a strong argument linking SO/spindle/coupling-locked brain activity with memory reactivation or consolidation.

We appreciate your suggestion regarding the lack of a pre- and post-sleep memory task in our study design. We acknowledge that, in the absence of behavioral measures, it is hard to directly link SO-spindle coupling to memory consolidation in an outcome-driven manner. Our interpretation is instead based on the well-established role of these oscillations in memory processes, as demonstrated in previous studies. We sincerely appreciate this feedback and will adjust our Discussion accordingly to reflect a more precise interpretation of our findings.

Discussion, Page 18 Lines 333-341

“Despite providing new insights, our study has several limitations. First, our scalp EEG did not directly capture hippocampal ripples, preventing us from conclusively demonstrating triple coupling. Second, the combination of EEG-fMRI and the lack of a memory task limit our ability to parse fine-grained BOLD responses at the DOWN- vs. UP-states of SOs and link observed activations to behavioral outcomes. Third, the use of large anatomical ROIs may mask subregional contributions of specific thalamic nuclei or hippocampal subfields. Finally, without a memory task, we cannot establish a direct behavioral link between sleep-rhythm-locked activation and memory consolidation. Future studies combining techniques such as ultra-high-field fMRI or iEEG with cognitive tasks may refine our understanding of subregional network dynamics and functional significance during sleep.”

(2) Relatedly, to understand the functional implications of the sleep rhythm-locked brain activity, the authors employed the "open-ended cognitive state decoding" method. While this method is interesting, it is rather indirect given that there were no behavioral indices in the manuscript. Thus, discussions based on these analyses are speculative at best. Please either tone down the language or find additional evidence to support these claims.

Moreover, the results from this method are difficult to understand. Figure 3e showed that for all three types of sleep events (SO, spindle, SO-spindle), the same mental states (e.g., working memory, episodic memory, declarative memory) showed opposite directions of activation (left and right panels showed negative and positive activation, respectively). How to interpret these conflicting results? This ambiguity is also reflected by the term used: declarative memory and episodic memories are both indexed in the results. Yet these two processes can be largely overlapped. So which specific memory processes do these brain activity patterns reflect? The Discussion shall discuss these results and the limitations of this method.

We appreciate your critical assessment of the open-ended cognitive state decoding method and its interpretational challenges. Given the concerns about the indirectness of this approach, we decided to remove its related content and results from Figure 3 in the main text and include it in Supplementary Figure 7.

Due to the complexity of memory-related processes, we acknowledge that distinguishing between episodic and declarative memory based solely on this approach is not straightforward. We will revise the Supplementary Materials to explicitly discuss these limitations and clarify that our findings do not isolate specific cognitive processes but rather suggest general associations with memory-related networks.

Discussion, Page 17-18 Lines 323-332

“To explore functional relevance, we employed an open-ended cognitive state decoding approach using meta-analytic data (NeuroSynth: Yarkoni et al. (2011)). Although this method usefully generates hypotheses about potential cognitive processes, particularly in the absence of a pre- and post-sleep memory task, it is inherently indirect. Many cognitive terms showed significant associations (16 of 50), such as “episodic memory,” “declarative memory,” and “working memory.” We focused on episodic/declarative memory given the known link with hippocampal reactivation (Diekelmann & Born, 2010; Staresina et al., 2015; Staresina et al., 2023). Nonetheless, these inferences regarding memory reactivation should be interpreted cautiously without direct behavioral measures. Future research incorporating explicit tasks before and after sleep would more rigorously validate these potenial functional claims.”

(3) The coupling strength is somehow inconsistent with prior results (Hahn et al., 2020, eLife, Helfrich et al., 2018, Neuron). Specifically, Helfrich et al. showed that among young adults, the spindle is coupled to the peak of the SO. Here, the authors reported that the spindles were coupled to down-to-up transitions of SO and before the SO peak. It is possible that participants' age may influence the coupling (see Helfrich et al., 2018). Please discuss the findings in the context of previous research on SO-spindle coupling.

We appreciate your concern regarding the temporal characteristics of SO-spindle coupling. We acknowledge that the SO-spindle coupling phase results in our study are not identical to those reported by Hahn et al. (2020); Helfrich et al. (2018). However, these differences may arise due to slight variations in event detection parameters, which can influence the precise phase estimation of coupling. Notably, Hahn et al. (2020) also reported slight discrepancies in their group-level coupling phase results, highlighting that methodological differences can contribute to variability across studies. Furthermore, our findings are consistent with those of Schreiner et al. (2021), further supporting the robustness of our observations.

That said, we acknowledge that our original description of SO-spindle coupling as occurring at the "transition from the lower state to the upper state" was not entirely precise. The -π/2 phase represents the true transition point, while our observed coupling phase is actually closer to the SO peak rather than strictly at the transition. We will revise this statement in the manuscript to ensure clarity and accuracy in describing the coupling phase.

Discussion, Page 16 Lines 283-291

“Our data provide insights into the neurobiological underpinnings of these sleep rhythms. SOs, originating mainly in neocortical areas such as the mPFC, alternate between DOWN- and UP-states. The thalamus generates sleep spindles, which in turn couple with SOs. Our finding that spindle peaks consistently occurred slightly before the UP-state peak of SOs (in 83 out of 107 participants), concurs with prior studies, including Schreiner et al. (2021). Yet it differs from some results suggesting spindles might peak right at the SO UP-state (Hahn et al., 2020; Helfrich et al., 2018). Such discrepancies could arise from differences in detection algorithms, participant age (Helfrich et al., 2018), or subtle variations in cortical-thalamic timing. Nonetheless, these results underscore the importance of coordinated SO-spindle interplay in supporting sleep-dependent processes.”

(4) The discussion is rather superficial with only two pages, without delving into many important arguments regarding the possible functional significance of these results. For example, the author wrote, "This internal processing contrasts with the brain patterns associated with external tasks, such as working memory." Without any references to working memory, and without delineating why WM is considered as an external task even working memory operations can be internal. Similarly, for the interesting results on SO and reduced DMN activity, the authors wrote "The DMN is typically active during wakeful rest and is associated with self-referential processes like mind-wandering, daydreaming, and task representation (Yeshurun, Nguyen, & Hasson, 2021). Its reduced activity during SOs may signal a shift towards endogenous processes such as memory consolidation." This argument is flawed. DMN is active during self-referential processing and mind-wandering, i.e., when the brain shifts from external stimuli processing to internal mental processing. During sleep, endogenous memory reactivation and consolidation are also part of the internal mental processing given the lack of external environmental stimulation. So why during SO or during memory consolidation, the DMN activity would be reduced? Were there differences in DMN activity between SO and SO-spindle coupling events?

We appreciate your concerns regarding the brevity of the discussion and the need for clearer theoretical arguments. We will expand this section to provide more in-depth interpretations of our findings in the context of prior literature. Regarding working memory (WM), we acknowledge that our phrasing was ambiguous. We will modify this statement in the Discussion section.

For the SO-related reduction in DMN activity, we recognize the need for a more precise explanation. This reduced DMN activity may reflect large-scale neural inhibition characteristic of the SO trough. The DMN is typically active during internally oriented cognition (e.g., self-referential processing or mind-wandering) and is suppressed during external stimuli processing (Yeshurun, Nguyen, & Hasson, 2021). It is unlikely, however, that this suppression of DMN during SO events is related to a shift from internal cognition to external responses given it is during deep sleep time. Instead, it could be driven by the inherent rhythmic pattern of SOs, which makes it difficult to separate UP- from DOWN-states (the two temporal regressors were highly correlated, and similar brain activation during SOs events was obtained if modelled at the SO peak instead). Since the amplitude at the SO trough is consistently larger than that at the SO peak, the neural activation we detected may primarily capture the large-scale inhibition from DOWN-state.

To address your final question, we have conducted the additional post hoc comparison of DMN activity between isolated SOs and SO-spindle coupling events. Our results indicate that

DMN activation during SOs was significantly lower than during SO-spindle coupling (t₍₁₀₆₎ = -4.17, p < 1e-4). This suggests that SO-spindle coupling may involve distinct neural dynamics that partially re-engage DMN-related processes, possibly reflecting memory-related reactivation. We appreciate your constructive feedback and will integrate these expanded analyses and discussions into our revised manuscript.

Results, Page 11 Lines 199-208

“Spindles were correlated with positive activation in the thalamus (ROI analysis, t₍₁₀₆₎ = 15.39, p < 1e-4), the anterior cingulate cortex (ACC), and the putamen, alongside deactivation in the DMN (Fig. 3c). Notably, SO-spindle coupling was linked to significant activation in both the thalamus (ROI analysis, t₍₁₀₆₎ \= 3.38, p = 0.0005) and the hippocampus (ROI analysis, t₍₁₀₆₎ \= 2.50, p = 0.0070, Fig. 3d). However, no decrease in DMN activity was found during SO-spindle coupling, and DMN activity during SO was significantly lower than during coupling (ROI analysis, t₍₁₀₆₎ \= -4.17, p < 1e-4). For more detailed activation patterns, see Table S5-S7. We also varied the threshold used to detect SO events to assess its effect on hippocampal activation during SO-spindle coupling and observed that hippocampal activation remained significant when the percentile thresholds for SO detection ranged between 71% and 80% (see Fig. S6).”

Discussion, Page 17-18 Lines 308-332

“An intriguing aspect of our findings is the reduced DMN activity during SOs when modeled at the SO trough (DOWN-state). This reduced DMN activity may reflect large-scale neural inhibition characteristic of the SO trough. The DMN is typically active during internally oriented cognition (e.g., self-referential processing or mind-wandering) and is suppressed during external stimuli processing (Yeshurun, Nguyen, & Hasson, 2021). It is unlikely, however, that this suppression of DMN during SO events is related to a shift from internal cognition to external responses given it is during deep sleep time. Instead, it could be driven by the inherent rhythmic pattern of SOs, which makes it difficult to separate UP- from DOWN-states (the two temporal regressors were highly correlated, and similar brain activation during SOs events was obtained if modelled at the SO peak instead, Fig. S5). Since the amplitude at the SO trough is consistently larger than that at the SO peak, the neural activation we detected may primarily capture the large-scale inhibition from DOWN-state. Interestingly, no such DMN reduction was found during SO-spindle coupling, implying that coupling may involve distinct neural dynamics that partially re-engage DMN-related processes, possibly reflecting memory-related reactivation. Future research using high-temporal-resolution techniques like iEEG could clarify these possibilities.

To explore functional relevance, we employed an open-ended cognitive state decoding approach using meta-analytic data (NeuroSynth: Yarkoni et al. (2011)). Although this method usefully generates hypotheses about potential cognitive processes, particularly in the absence of a pre- and post-sleep memory task, it is inherently indirect. Many cognitive terms showed significant associations (16 of 50), such as “episodic memory,” “declarative memory,” and “working memory.” We focused on episodic/declarative memory given the known link with hippocampal reactivation (Diekelmann & Born, 2010; Staresina et al., 2015; Staresina et al., 2023). Nonetheless, these inferences regarding memory reactivation should be interpreted cautiously without direct behavioral measures. Future research incorporating explicit tasks before and after sleep would more rigorously validate these potential functional claims.”

Reviewing Editor Comment:

The reviewers think that you are working on a relevant and important topic. They are praising the large sample size used in the study. The reviewers are not all in line regarding the overall significance of the findings, but they all agree the paper would strongly benefit from some extra work, as all reviewers raise various critical points that need serious consideration.

We appreciate your recognition of the relevance and importance of our study, as well as your acknowledgment of the large sample size as a strength of our work. We understand that there are differing perspectives regarding the overall significance of our findings, and we value the constructive critiques provided. We are committed to addressing the key concerns raised by all reviewers, including refining our analyses, clarifying our interpretations, and incorporating additional discussions to strengthen the manuscript. Below, we address your specific recommendations and provide responses to each point you raised to ensure our methods and results are as transparent and comprehensible as possible. We believe that these revisions will significantly enhance the rigor and impact of our study, and we sincerely appreciate your thoughtful feedback in helping us improve our work.

Reviewer #1 (Recommendations for the authors):

(1) The phrase "overnight sleep" suggests an entire night, while these were rather "nocturnal naps". Please rephrase.

Thank you for pointing this out. We have revised the phrasing in our manuscript to "nocturnal naps" instead of "overnight sleep" to more accurately reflect the duration of the sleep recordings.

(2) Sleep staging results (macroscopic sleep architecture) should be provided in more detail (at least min and % of the different sleep stages, sleep onset latency, total sleep duration, total recording duration), at least mean/SD/range.

Thank you for this suggestion. We will provide comprehensive tables in the supplementary materials, contains descriptive information about sleep-related characteristics. This information will help provide a clearer overview of the macroscopic sleep architecture in our dataset.

Supplementary Materials, Page 42, Table S1

Author response table 1.

Descriptive results of demographic information and sleep characteristics. Note: The total recorded time is equal to the awake time plus the total sleep time. The sleep onset latency is the time taken to reach the first sleep epoch. The Sleep Efficiency is the ratio of actual sleep time to total recording time.

Reviewer #2 (Recommendations for the authors):

In order to allow for a better estimation of the reliability of the detected sleep events, please:

(1) Provide densities and absolute numbers of all detected SOs and spindles (N1, NREM, and REM sleep).

Thank you for pointing this out. We will provide comprehensive tables in the supplementary materials, contains detailed information about sleep waves at each sleep stage for all 107 subjects (Table S2-S4), listing for each subject:1) Different sleep stage duration; 2) Number of detected SOs; 3) Number of detected spindles; 4) Number of detected SO-spindle coupling events; 5) Density of detected SOs; 6) Density of detected spindles; 7) Density of detected SO-spindle coupling events.

Supplementary Materials, Page 43-54, Table S2-S4

(Consider of the length, we do not list all the tables here. Please refer to the revised manuscript.)

(2) Show ERPs for all detected SOs and spindles (per sleep stage).

Thank you for the suggestion. We will provide ERPs for all detected SOs and spindles, separated by sleep stage (N1, N2&N3, and REM) in supplementary Fig. S2-S4. These ERP waveforms will help illustrate the characteristic temporal profiles of SOs and spindles across different sleep stages.

Methods, Page 25, Line 525-532

“Event-related potentials (ERP) analysis. After completing the detection of each sleep rhythm event, we performed ERP analyses for SOs, spindles, and coupling events in different sleep stages. Specifically, for SO events, we took the trough of the DOWN-state of each SO as the zero-time point, then extracted data in a [-2 s to 2 s] window from the broadband (0.1–30 Hz) EEG and used [-2 s to -0.5 s] for baseline correction; the results were then averaged across 107 subjects (see Fig. S2a). For spindle events, we used the peak of each spindle as the zero-time point and applied the same data extraction window and baseline correction before averaging across 107 subjects (see Fig. S2b). Finally, for SO-spindle coupling events, we followed the same procedure used for SO events (see Fig. 2a, Figs. S3–S4).”

Supplementary Materials, Page 36-38, Fig. S2-S4

Author response image 1.

ERPs of SOs and spindles coupling during different sleep stages across all 107 subjects. a. ERP of SOs in different sleep stages using the broadband (0.1–30 Hz) EEG data. We align the trough of the DOWN-state of each SO at time zero (see Methods for details). The orange line represents the SO ERP in the N1 stage, the black line represents the SO ERP in the N2&N3 stage, and the green line represents the SO ERP in the REM stage. b. ERP of spindles in different sleep stages using the broadband (0.1–30 Hz) EEG data. We align the peak of each spindle at time zero (see Methods for details). The color scheme is the same as in panel a.

Author response image 2.

ERP and time-frequency patterns of SO-spindle coupling in the N1 stage. The averaged temporal frequency pattern and ERP across all instances of SO-spindle coupling, computed over all subjects, following the same procedure as in Fig. 2a, but for N1 stage.

Author response image 3.

ERP and time-frequency patterns of SO-spindle coupling in the REM stage. The averaged temporal frequency pattern and ERP across all instances of SO-spindle coupling, computed over all subjects, again following the same procedure as in Fig. 2a, but for REM stage.

(3) Provide detailed info concerning sleep characteristics (time spent in each sleep stage etc.).

Thank you for this suggestion. Same as the response above, we will provide comprehensive tables in the supplementary materials, contains descriptive information about sleep-related characteristics.

Supplementary Materials, Page 42, Table S1 (same as above)

(4) What would happen if more stringent parameters were used for event detection? Would the authors still observe a significant number of SO spindles during N1 and REM? Would this affect the fMRI-related results?

Thank you for this suggestion. Our methods for detecting SOs, spindles, and their couplings were originally developed for N2 and N3 sleep data, based on the specific characteristics of these stages. These methods are widely recognized in sleep research (Hahn et al., 2020; Helfrich et al., 2019; Helfrich et al., 2018; Ngo, Fell, & Staresina, 2020; Schreiner et al., 2022; Schreiner et al., 2021; Staresina et al., 2015; Staresina et al., 2023). However, because this percentile-based detection approach will inherently identify a certain number of events if applied to other stages (e.g., N1 and REM), the nature of these events in those stages remains unclear compared to N2/N3. We nevertheless identified and reported the detailed descriptive statistics of these sleep rhythms in all sleep stages, under the same operational definitions, both for completeness and as a sanity check. Within the same subject, there should be more SOs, spindles, and their couplings in N2/N3 than in N1 or REM (see also Figure S2-S4, Table S1-S4).

Furthermore, in order to explore the impact of this on our fMRI results, we conducted an additional sensitivity analysis by applying different detection parameters for SOs. Specifically, we adjusted amplitude percentile thresholds for SO detection (the parameter that has the greatest impact on the results). We used the hippocampal activation value during N2&N3 stage SO-spindle coupling as an anchor value and found that when the parameters gradually became stricter, the results were similar to or even better than the current results. However, when we continued to increase the threshold, the results began to gradually decrease until the threshold was increased to 80%, and the results were no longer significant. This indicates that our results are robust within a specific range of parameters, but as the threshold increases, the number of trials decreases, ultimately weakening the statistical power of the fMRI analysis.

Thank you again for your suggestions on sleep rhythm event detection. We will add the results in Supplementary and revise our manuscript accordingly.

Results, Page 11, Line 199-208

“Spindles were correlated with positive activation in the thalamus (ROI analysis, t₍₁₀₆₎ = 15.39, p < 1e-4), the anterior cingulate cortex (ACC), and the putamen, alongside deactivation in the DMN (Fig. 3c). Notably, SO-spindle coupling was linked to significant activation in both the thalamus (ROI analysis, t₍₁₀₆₎ \= 3.38, p = 0.0005) and the hippocampus (ROI analysis, t₍₁₀₆₎ \= 2.50, p = 0.0070, Fig. 3d). However, no decrease in DMN activity was found during SO-spindle coupling, and DMN activity during SO was significantly lower than during coupling (ROI analysis, t₍₁₀₆₎ \= -4.17, p < 1e-4). For more detailed activation patterns, see Table S5-S7. We also varied the threshold used to detect SO events to assess its effect on hippocampal activation during SO-spindle coupling and observed that hippocampal activation remained significant when the percentile thresholds for SO detection ranged between 71% and 80% (see Fig. S6).”

Supplementary Materials, Page 40, Fig. S6

Author response image 4.

Influence of the percentile threshold for SO detection on hippocampal activation (ROI) during SO-spindle coupling. We changed the percentile threshold for SO event detection in the EEG data analysis and then reconstructed the GLM design matrix based on the SO events detected at each threshold. The brain-wide activation pattern of SO-spindle couplings in the N2/3 stage was extracted using the same method as shown in Fig. 3. The gray horizontal line represents the significant range (71%–80%). * p < 0.05.

Finally, we sincerely thank all again for your thoughtful and constructive feedback. Your insights have been invaluable in refining our analyses, strengthening our interpretations, and improving the clarity and rigor of our manuscript. We appreciate the time and effort you have dedicated to reviewing our work, and we are grateful for the opportunity to enhance our study based on your recommendations.

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Author response:

We kindly thank the senior editor, the reviewing editor, and the esteemed reviewers for their invaluable insights in enhancing our manuscript. The assessment and feedback, particularly on the role of directly released bacterial ATP versus OMV-delivered bacterial ATP and its role on neutrophils, addressing study limitations, and discussing our models is highly appreciated.

The points you raised let us critically rethink our approach, our results, and our conclusions. Furthermore, it gave us the chance to elaborate on some critical aspects that you mentioned. With your help, we will make clarifications throughout the manuscript, and we will add the data about neutrophil numbers in the different organs (reviewer #1, weaknesses #3).

Reviewer #1 (Public Review):

Summary:

• Extracellular ATP represents a danger-associated molecular pattern associated to tissue damage and can act also in an autocrine fashion in macrophages to promote proinflammatory responses, as observed in a previous paper by the authors in abdominal sepsis. The present study addresses an important aspect possibly conditioning the outcome of sepsis that is the release of ATP by bacteria. The authors show that sepsis-associated bacteria do in fact release ATP in a growth dependent and strain-specific manner. However, whether this bacterial derived ATP play a role in the pathogenesis of abdominal sepsis has not been determined. To address this question, a number of mutant strains of E. coli has been used first to correlate bacterial ATP release with growth and then, with outer membrane integrity and bacterial death. By using E. coli transformants expressing the ATP-degrading enzyme apyrase in the periplasmic space, the paper nicely shows that abdominal sepsis by these transformants results in significantly improved survival. This effect was associated with a reduction of peritoneal macrophages and CX3CR1+ monocytes, and an increase in neutrophils. To extrapolate the function of bacterial ATP from the systemic response to microorganisms, the authors exploited bacterial OMVs either loaded or not with ATP to investigate the systemic effects devoid of living microorganisms. This approach showed that ATP-loaded OMVs induced degranulation of neutrophils after lysosomal uptake, suggesting that this mechanism could contribute to sepsis severity.

Strengths:

• A strong part of the study is the analysis of E. coli mutants to address different aspects of bacterial release of ATP that could be relevant during systemic dissemination of bacteria in the host.

We want to thank the reviewer for recognizing this important aspect of our experimental approach.

Weaknesses:

• As pointed out in the limitations of the study whether ATP-loaded OMVs provide a mechanistic proof of the pathogenetic role of bacteria-derived ATP independently of live microorganisms in sepsis is interesting but not definitively convincing. It could be useful to see whether degranulation of neutrophils is differentially induced by apyrase-expressing vs control E. coli transformants.

We thank the reviewer for raising several important points. In our study, we assessed local and systemic effects of released bacterial ATP. The consequences of local bacterial ATP release were assessed using an apyrase-expressing E. coli transformant. Locally, bacterial ATP resulted in a decrease in neutrophil numbers and we hypothesize that directly released bacterial ATP either leads to neutrophil death (e.g. via P2X7 receptor (Proietti et al., 2019)) or interferes with the recruitment of neutrophils (e.g. via P2Y receptors (Junger, 2011)).

The systemic consequences were assessed using ATP-loaded and empty OMV. We have shown that degranulation is induced by OMV-derived bacterial ATP. ATP-containing OMV are engulfed by neutrophils, reach its endolysosomal compartment and might activate purinergic receptors, which then lead to aberrant degranulation. This concept, that needs to be explored in future studies, is fundamentally different from classical purinergic signaling via directly released bacterial ATP into the extracellular space.

It is possible that neutrophil degranulation is also modulated by directly released bacterial ATP. We agree that this should be assessed in future studies. Also, the role of OMV-derived bacterial ATP should be assessed locally as well as the importance of directly released vs. OMV-mediated bacterial ATP dissected locally. Based on our measurements (Figure 4-figure supplement 1A and Figure 5C), we estimate that the effect of OMV-derived bacterial ATP might be much smaller than the effects of directly released bacterial ATP. Thus, direct ATP release might predominate locally. However, we fully agree that this has to be investigated in a future study to reconcile the different aspects of bacterial ATP signaling. A paragraph will be added to the manuscript, in which we discuss this particular issue.

• Also, the increase of neutrophils in bacterial ATP-depleted abdominal sepsis, which has better outcomes than "ATP-proficient" sepsis, seems difficult to correlate to the hypothesized tissue damage induced by ATP delivered via non-infectious OMVs.

We fully acknowledge the mentioned discrepancy. What we propose is that bacterial ATP exhibits different functions that are dependent on the release mechanism (see above). Locally, in the peritoneal cavity, neutrophil numbers are decreased by directly released bacterial ATP. Remotely, ATP is delivered via OMV and impacts on neutrophil function. We agree that, in particular, in the peritoneal cavity, both effects may play a role. However, the impact of directly released bacterial ATP seems to be dominant (see above).

We propose that neutrophils are decreased locally because of directly released bacterial ATP, which prevents efficient infection control and, therefore, impairs sepsis survival. In addition, these fewer neutrophils might even be dysregulated by the engulfment of bacterial ATP delivered via OMV, which leads to an upregulated and possibly aberrant degranulation process worsening local and remote tissue damage. We agree that in addition to neutrophil numbers, the function of local neutrophils should be assessed with and without the influence of OMV-delivered bacterial ATP. This could be done by RNA sequencing of primary neutrophils from the peritoneal cavity or neutrophil cell lines as well as degranulation assays.

• Are the neutrophils counts affected by ATP delivered via OMVs?

This is difficult to show in the peritoneal cavity where we have both, directly released bacterial ATP and OMV-derived bacterial ATP. We assessed such putative difference, however, for the systemic organs and the blood, where we did not find any differences in neutrophil numbers. We will include the figure in the revised manuscript as Figure 6-figure supplement 3C.

Author response image 1.

• A comparison of cytokine profiles in the abdominal fluids of E. coli and OMV treated animals could be helpful in defining the different responses induced by OMV-delivered vs bacterial-released ATP. The analyses performed on OMV treated versus E. coli infected mice are not closely related and difficult to combine when trying to draw a hypothesis for bacterial ATP in sepsis.

We fully agree that there are several open questions that remain to be elucidated, in particular, to differentiate the local role of directly released versus OMV-delivered bacterial ATP. In this study, we laid the foundation for future in vivo research to examine the specific role of bacterial ATP in sepsis. Such future research avenues might be to investigate the local effects of OMV-delivered bacterial ATP, and how neutrophil migration, apoptosis and degranulation are altered. We agree that exploration of the local secretory immune response and cytokine profiles are relevant to understand the different mechanisms of how bacterial ATP alters sepsis. However, such experiments should be ideally performed in systems where the source and the delivery of ATP can be modulated locally.

• Also it was not clear why lung neutrophils were used for the RNAseq data generation and analysis.

Thank you for this remark. We have chosen primary lung neutrophils for four reasons:

(1) Isolation of primary lung neutrophils allowed us to assess an in vivo response that would not have been possible with cell lines.

(2) The lung and the respiratory system are among the clinically most important organs affected during sepsis resulting in a significant cause of mortality.

(3) We show in Figure 6C that specifically in the lung, OMV are engulfed by neutrophils, which shows the relevance of the lung also in our study context.

(4) And finally, lung neutrophils were chosen to examine specifically distant and not local effects.

Reviewer #2 (Public Review):

Summary:

• In their manuscript "Released Bacterial ATP Shapes Local and Systemic Inflammation during Abdominal Sepsis", Daniel Spari et al. explored the dual role of ATP in exacerbating sepsis, revealing that ATP from both host and bacteria significantly impacts immune responses and disease progression.

Strengths:

• The study meticulously examines the complex relationship between ATP release and bacterial growth, membrane integrity, and how bacterial ATP potentially dampens inflammatory responses, thereby impairing survival in sepsis models. Additionally, this compelling paper implies a concept that bacterial OMVs act as vehicles for the systemic distribution of ATP, influencing neutrophil activity and exacerbating sepsis severity.

We thank the reviewer for mentioning these key points and supporting the relevance of our study.

Weaknesses:

(1) The researchers extracted and cultivated abdominal fluid on LB agar plates, then randomly picked 25 colonies for analysis. However, they did not conduct 16S rRNA gene amplicon sequencing on the fluid itself. It is worth noting that the bacterial species present may vary depending on the individual patients. It would be beneficial if the authors could specify whether they've verified the existence of unculturable species capable of secreting high levels of Extracellular ATP.

Most septic complications are caused by a limited spectrum of bacteria, belonging mainly either to the Firmicutes or the Proteobacteria phyla, including E. coli, K. pneumoniae, S. aureus or E. faecalis (Diekema et al., 2019; Mureșan et al., 2018). We validated this well documented existing evidence by randomly assessing 25 colonies. For the planned experiments, it was crucial to work with culturable bacteria; otherwise, ATP measurements, the modulation of ATP generation or loading of OMV would not have been possible. Using such culturable bacteria allowed us to describe mechanisms of ATP release.

We fully agree that hard-to-culture or unculturable bacteria might contribute significantly to septic complications. This, however, would need to be explored in future studies using extensive culturing methods (Cheng et al., 2022).

(2) Do mice lacking commensal bacteria show a lack of extracellular ATP following cecal ligation puncture?

ATP is typically secreted by many cells of the host in active and passive manners in the case of any injury, including cecal ligation and puncture (Burnstock, 2016; Dosch et al., 2018; Eltzschig et al., 2012; Idzko et al., 2014). We hypothesize that bacterial ATP is a potential priming agent at early stages of sepsis, and indeed, at such early time points, a comparison of peritoneal ATP levels between germfree and colonized mice could support our hypothesis. Future studies addressing this question must, however, correct for the different immune responses between germ-free and colonized mice. This is of utmost importance, especially for the cecal ligation and puncture model, since the cecum of germ-free mice is extremely large, making such experiments hard to control.

(3) The authors isolated various bacteria from abdominal fluid, encompassing both Gram-negative and Gram-positive types. Nevertheless, their emphasis appeared to be primarily on the Gram-negative E. coli. It would be beneficial to ascertain whether the mechanisms of Extracellular ATP release differ between Gram-positive and Gram-negative bacteria. This is particularly relevant given that the Gram-positive bacterium E. faecalis, also isolated from the abdominal fluid, is recognized for its propensity to release substantial amounts of Extracellular ATP.

We fully agree with this comment. In this paper, we used E. coli as our model organism to determine the principles of sepsis-associated bacterial ATP release and therefore focused on gram-negative bacteria. In addition to the direct, growth-dependent release, we found a relevant impact of OMV-delivered bacterial ATP. For this latter purpose, a gram-negative strain, in which OMV generation has been well described (Schwechheimer & Kuehn, 2015), was chosen. Recently, gram-positive bacteria have been shown to secrete ATP and OMV as well (Briaud & Carroll, 2020; Hironaka et al., 2013; Iwase et al., 2010). Given the fundamental differences in the structure of the cell wall of gram-positive bacteria and the mechanisms of OMV generation and release, future studies are required to assess the relevance of directly released and OMV-delivered ATP in gram-positive bacteria.

(4) The authors observed changes in the levels of LPM, SPM, and neutrophils in vivo. However, it remains uncertain whether the proliferation or migration of these cells is modulated or inhibited by ATP receptors like P2Y receptors. This aspect requires further investigation to establish a convincing connection.

We fully agree with this comment. The decrease in LPM and the consequential predomination of SPM have been well described after inflammatory stimuli in the context of the macrophage disappearance reaction (Ghosn et al., 2010). Also, it has been shown that purinergic signaling modulates infiltration of neutrophils and can lead to cell death as a consequence of P2Y and P2X receptor activation (Junger, 2011; Proietti et al., 2019). In our study, we propose that intracellular purinergic receptors contribute to neutrophil function during sepsis. After introducing the general principles and fundaments of bacterial ATP with our studies, we fully agree that additional experiments need to address downstream purinergic receptor activation. That, however, would go beyond the scope of our study.

(5) Additionally, is it possible that the observed in vivo changes could be triggered by bacterial components other than Extracellular ATP? In this research field, a comprehensive collection of inhibitors is available, so it is desirable to utilize them to demonstrate clearer results.

This question is of utmost importance and defined the choice of our model and experimental approach. When we started the project, we used two different E. coli mutants that release low (ompC) and high (eaeH) amounts of ATP. However, the limitation of this approach is that these are different bacteria, which may also differ in the components they secrete or the surface proteins they express. We, therefore, decided against that approach. With the approach we finally used (same bacterium, just with and without ATP), we aimed to minimize the influence of non-ATP bacterial components.

(6) Have the authors considered the role of host-derived Extracellular ATP in the context of inflammation?

Yes, the role of host-derived extracellular ATP in inflammation and sepsis is well-established with contradictory results (Csóka et al., 2015; Ledderose et al., 2016). This conflicting data was the rationale to test the relevance of bacterial ATP. We suggest that bacterial ATP is essential in the early phase of sepsis when bacteria invade the sterile compartment and before efficient host response, including the eukaryotic release of ATP, is established.

(7) The authors mention that Extracellular ATP is rapidly hydrolyzed by ectonucleotases in vivo. Are the changes of immune cells within the peritoneal cavity caused by Extracellular ATP released from bacterial death or by OMVs?

This is a relevant question that was also asked by reviewer #1, and we answered it in detail above (weaknesses comment #1 and #2). From our ATP measurements (Figure 4-figure supplement 1A and Figure 5C), we conclude that locally, the role of directly released bacterial ATP (extracellular) predominates over OMV-derived bacterial ATP. Furthermore, the mechanisms between directly released and OMV-derived bacterial ATP (within OMV, engulfed and transported to the endolysosomal compartment) are different, and especially extracellular ATP has been described to lead to apoptosis via P2X7 signaling.

(8) In the manuscript, the sample size (n) for the data consistently remains at 2. I would suggest expanding the sample size to enhance the robustness and rigor of the results.

Two biological replicates (independent cultures) were only used for the bacteria cultures in Figure 1, Figure 2, and Figure 3, which achieved similar results and the standard deviation remained very small, indicating its robustness. In the in vitro experiments in Figure 5 we used a sample size of 6 (three biological replicates measured in technical duplicates), since we saw bigger deviations in our measurements. For the in vivo experiments, we always used 5 or more animals in at least two independent experiments.

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Author Response

We would like to thank the reviewers for providing constructive feedback on the manuscript. To address the weaknesses identified, we are performing additional experiments and generating additional data, to be added to the updated manuscript.

(1) The utility of a pipeline depends on the generalization properties.

While the proposed pipeline seems to work for the data the authors acquired, it is unclear if this pipeline will actually generalize to novel data sets possibly recorded by a different microscope (e.g. different brand), or different imagining conditions (e.g. illumination or different imagining artifacts) or even to different brain regions or animal species, etc.

The authors provide a 'black-box' approach that might work well for their particular data sets and image acquisition settings but it is left unclear how this pipeline is actually widely applicable to other conditions as such data is not provided.

In my experience, without well-defined image pre-processing steps and without training on a wide range of image conditions pipelines typically require significant retraining, which in turn requires generating sufficient amounts of training data, partly defying the purpose of the pipeline. It is unclear from the manuscript, how well this pipeline will perform on novel data possibly recorded by a different lab or with a different microscope.

To address generalizability, we are performing several validation experiments with data from different 1) channels, 2) species (rat), and 3) microscopes, to highlight the robustness of our deep learning (DL) segmentation model to out-of-distribution data with different characteristics and acquisition protocols. We first used our model to segment three images (507x507 x&y, 250-170 um z) from three C57BL/6 mice acquired on the same two-photon fluorescent microscope following the same imaging protocol. The vasculature was labelled with the Texas Red dextran, as in the current experiment. In place of the EYFP signal from pyramidal neurons (2nd channel), gaussian noise was generated with a mean and standard deviation identical to the acquired vascular channel. A second set of two images(507x507 x&y, 300-400 um z) from two Fischer rats with Alexa680-dextran label in the plasma; these rats were imaged on the same two-photon fluorescence microscope, but with galvano scanners (instead of resonant scanners). A second channel of random Gaussian noise was also added here. Finally, an image of vasculature from a ex-vivo cleared mouse brain (1665x1205x780 um) imaged on a light sheet fluorescence microscope (Miltenyi UltraMicroscope Blaze) was also segmented with our model. Lectin-DyLight 649 was used to label the vasculature in this cohort. The Dice Score, Precision, Recall, Hausdorff 95%, and Mean surface distance will be reported for all of these additional image segmentations, upon generation of ground truth images. Finally, examples of the generated segmentation masks are presented in Author response image 1 for visual comparison. Of final note, should the segmentation results on a new data set be unsatisfactory, the methods downstream from segmentation are still applicable and the model can be further fine-tuned on other out-of-distribution data.

Author response image 1.

Examples of the deep learning model output on out of distribution data from a different mouse strain, from a different species (Fischer rat), and on a different microscope using a different imaging modality.

(2) Some of the chosen analysis results seem to not fully match the shown data, or the visualization of the data is hard to interpret in the current form.

We are updating the visualizations to make them more accessible and we will ensure matching between tables and figures.

(3) Additionally, some measures seem not fully adapted to the current situation (e.g. the efficiency measure does not consider possible sources or sinks). Thus, some additional analysis work might be required to account for this.

Thank you for your comment. The efficiency metric was selected as it does not consider sources or sinks. We do agree that accounting for vessel subtypes in the analysis (thus classifying larger vessels as either supplying or draining) would be uniquely useful: notwithstanding, it is extremely laborious. We are therefore leveraging machine learning in a parallel project to afford vessel classification by subtype. The source/sink analysis is also confounded by the small field-of-view of in situ 2PFM. Future work will investigate network remodelling across the whole brain with ex-vivo light sheet fluorescence microscopy.

(4) The authors apply their method to in vivo data. However, there are some weaknesses in the design that make it hard to accept many of the conclusions and even to see that the method could yield much useful data with this type of application. Primarily, the acquisition of a large volume of tissue is very slow. In order to obtain a network of vascular activity, large volumes are imaged with high resolution. However, the volumes are scanned once every 42 seconds following stimulation. Most vascular responses to neuronal activation have come and gone in 42 seconds so each vessel segment is only being sampled at a single time point in the vascular response. So all of the data on diameter changes are impossible to compare since some vessels are sampled during the initial phase of the vascular response, some during the decay, and many probably after it has already returned to baseline. The authors attempt to overcome this by alternating the direction of the scan (from surface to deep and vice versa). But this only provides two sample points along the vascular response curve and so the problem still remains.

We thank the Reviewer for bringing up this important point.

Although vessels can show relatively rapid responses to perturbation, vascular responses to photostimulation of ChannelRhodopsin-2 in neighbouring neurons are typically long lasting: they do not come and go in 42 seconds. To demonstrate this point, we acquired higher temporal-resolution images of smaller volumes of tissue over 5 minutes preceding and following the 5-s photoactivation with the original parameters. Imaging protocol was different in that we utilized a piezoelectric motor, smaller field of view, and only 3x frame averaging, resulting in a temporal resolution of 1.57-2.63 seconds. This acquisition was repeated at 4 different cortical depths (325 um, 250 um, 150um, and 40 um) in a single mouse.The vascular radii were estimated using our presented pipeline. Raw data and LOESS fits are shown in Author response image 2 (below). Vessels shorter than 20 um in length were excluded from the analysis. A video of one of the acquisitions is shown along with the timecourses of select vessels’ caliber changes in Author response image 3. The vascular caliber changes following photostimulation persisted for several minutes, consistent with earlier observations by us and others1–4. These higher temporal-resolution scans of smaller tissue volumes will be repeated in two more mice; we will therein assess the repeatability of individual vessel responses to repeated stimulations.

Author response image 2.

A. The vascular radii of multiple vessels were imaged at 4 different cortical depths, each within a 507 x (75-150) x (30-45)um tissue volume. Baseline scanning lasted for 5 minutes, followed by 5 seconds of blue or green light stimulation at 4.3 mW/mm2, and culminating in 5 minutes of post-stimulation scanning. B. LOESS fits of the vessel radius estimates for each vessel segment identified.

Author response image 3.

Estimated vascular radius at each timepoint for select vessels from the imaging stack shown in the following video: https://flip.com/s/kB1eTwYzwMJE

(5) A second problem is the use of optogenetic stimulation to activate the tissue. First, it has been shown that blue light itself can increase blood flow (Rungta et al 2017). The authors note the concern about temperature increases but that is not the same issue. The discussion mentions that non-transgenic mice were used to control for this with "data not shown". This is very important data given these earlier reports that have found such effects and so should be included.

We will update the manuscript to incorporate the data on volumetric scanning in nontransgenic C57BL/6 mice undergoing blue light stimulation, with identical parameters as those used in Thy-ChR2 mice. As before, responders were identified as vessels that following blue light stimulation show a radius change greater than 2 standard deviations of their baseline radius standard deviation: their estimated radii changes are shown in Author response image 4 below. There were no statistical difference between radii distributions of any of the photostimulation conditions and pre-photostimulation baseline. A comparison of this with the transgenic THY1-ChR2-EYFP mice will be included in manuscript updates.

Author response image 4.

Radius change measurements for responding vessels from the Thy1-ChR2 mice described in the manuscript (top row) vs. 4 wild-type C57BL6/J mice (bottom row). Response to photostimulation was defined as a change above twice their baseline standard deviation. 458nm light was applied at 1.1 mW/mm^2 and 4.3 mW/mm^2; while 552 nm light was applied at 4.3 mW/mm^2. No statistically significant differences were observed between the radii distributions in any condition, Wilcoxon test, Bonferroni correction.

(6) Secondly, there doesn't seem to be any monitoring of neural activity following the photo-stimulation. The authors repeatedly mention "activated" neurons and claim that vessel properties change based on distance from "activated" neurons. But I can't find anything to suggest that they know which neurons were active versus just labeled. Third, the stimulation laser is focused at a single depth plane. Since it is single-photon excitation, there is likely a large volume of activated neurons. But there is no way of knowing the spatial arrangement of neural activity and so again, including this as a factor in the analysis of vascular responses seems unjustified.

Given the high fidelity of Channel-Rhodpsin2 activation with blue light, we assume that all labeled neurons within the volume of photostimulation are being activated. Depending on their respective connectivities, their postsynaptic neurons (whether or not they are labelled) are also activated. We indeed agree with the reviewer that the spatial distribution of neuronal activation is not well defined. We will revise the manuscript to update the terminology from activated to labeled neurons and stress in the Discussion that the motivation for assessing the distance to the closest labelled neuron as one of our metrics is purely to demonstrate the possibility of linking vascular response to activations in some of their neighbouring neurons and including morphological metrics in the computational pipeline. Of final note, the depth-dependence of the distance between labelled neurons and responding vessels can also readily be assessed using our computational pipeline.

(7) The study could also benefit from more clear illustration of the quality of the model's output. It is hard to tell from static images of 3-D volumes how accurate the vessel segmentation is. Perhaps some videos going through the volume with the masks overlaid would provide some clarity. Also, a comparison to commercial vessel segmentation programs would be useful in addition to benchmarking to the ground truth manual data.

We generated a video demonstrating the deep-learning model outputs and have made the video available here: https://flip.com/s/_XBs4yVxisNs Additional videos will be uploaded.

(8) Another useful metric for the model's success would be the reproducibility of the vessel responses. Seeing such a large number of vessels showing constrictions raises some flags and so showing that the model pulled out the same response from the same vessels across multiple repetitions would make such data easier to accept.

We have generated a figure demonstrating the repeatability of the vascular responses following photoactivation in a volume, and presented them next to the corresponding raw acquisitions for visual inspection. It is important to note that there is a significant biological variability in vessels’ responses to repeated stimulation, as described previously 2,5. Constrictions have been reported in the literature by our group and others 1,3,4,6,7, though their prevalence has not been systematically studied to date. Concerning the reproducibility of our analysis, we will demonstrate model reproducibility (as a metric of its success) in the updated manuscript.

Author response image 5.

Registered acquisitions of the vasculature before and after optogenetic stimulation for 5 scan pairs over 3 different stimulation conditions. The estimated radii along vessel segments are presented.

Author response image 6.

Sample capillaries constrictions from maximum intensity projections at repeated timepoints following optogenetic stimulation. Baseline (pre-stimulation) image is shown on the left and the post-stimulation image, on the right, with the estimated radius changes listed to the left.

(9) A number of findings are questionable, at least in part due to these design properties. There are unrealistically large dilations and constrictions indicated. These are likely due to artifacts of the automated platform. Inspection of these results by eye would help understand what is going on.

Some of the dilations were indeed large in magnitude. We present select examples of large dilations and constrictions ranging in magnitude from 2.08 to 10.80 um for visual inspection (for reference, average, across vessel and stimuli, magnitude of radius changes were 0.32 +/- 0.54 um). Diameter changes above 5 um were visually inspected.

Author response image 7.

Additional views of diameter changes in maximum intensity projections ranging in magnitude from 2.08 um to 10.80 um.

(10) In Figure 6, there doesn't seem to be much correlation between vessels with large baseline level changes and vessels with large stimulus-evoked changes. It would be expected that large arteries would have a lot of variability in both conditions and veins much less. There is also not much within-vessel consistency. For instance, the third row shows what looks like a surface vessel constricting to stimulation but a branch coming off of it dilating - this seems biologically unrealistic.

We now plot photostimulation-elicited vesselwise radius changes vs. their corresponding baseline radius standard deviations (Author response image 8 below). The Pearson correlation between the baseline standard deviation and the radius change was 0.08 (p<1e-5) for 552nm 4.3 mW/mm^2 stimulation, -0.08 (p<1e-5) for 458nm 1.1 mW/mm^2 stimulation, and -0.04 (p<1e-5) for 458nm 4.3 mW/mm^2 stimulation. For non-control (i.e. blue) photostimulation conditions, the change in the radius is thus negatively correlated to the vessel’s baseline radius standard deviation. The within-vessel consistency is explicitly evaluated in Figure 8 of the manuscript. As for the instance of a surface vessel constricting while a downstream vessel dilates, it is important to remember that the 2PFM FOV restricts us to imaging a very small portion of the cortical microvascular network (one (among many) daughter vessels showing changes in the opposite direction to the parent vessel is not violating the conservation of mass).

Author response image 8.

A plot of the vessel radius change elicited by photostimulation vs. baseline radius standard deviation.

(11) As mentioned, the large proportion of constricting capillaries is not something found in the literature. Do these happen at a certain time point following the stimulation? Did the same vessel segments show dilation at times and constriction at other times? In fact, the overall proportion of dilators and constrictors is not given. Are they spatially clustered? The assortativity result implies that there is some clustering, and the theory of blood stealing by active tissue from inactive tissue is cited. However, this theory would imply a region where virtually all vessels are dilating and another region away from the active tissue with constrictions. Was anything that dramatic seen?

The kinetics of the vascular responses are not accessible via the current imaging protocol and acquired data; however, this computational pipeline can readily be adapted to test hypotheses surrounding the temporal evolution of the vascular responses, as shown in Author response image 2 (with higher temporal-resolution data). Some vessels dilate at some time points and constrict at others as shown in Author response image 2. As listed in Table 2, 4.4% of all vessels constrict and 7.5% dilate for 452nm stimulation at 4.3 mW/mm^2. There was no obvious spatial clustering of dilators or constrictors: we expect such spatial patterns to more likely result from different modes of stimulation and/or in the presence of a pathology. The assortativity peaked at 0.4 (i.e. is quite far from 1 where each vessel’s response exactly matches that of its neighbour).

(12) Why were nearly all vessels > 5um diameter not responding >2SD above baseline? Did they have highly variable baselines or small responses? Usually, bigger vessels respond strongly to local neural activity.

In Author response image 9, we now present the stimulation-induced radius changes vs. baseline radius variability across vessels with a radius greater than 5 um. The Pearson correlation between the radius change and the baseline radius standard deviation was 0.04 (p=0.5) for 552nm 4.3 mW/mm^2 stimulation, -0.26 (p<1e-5) for 458nm 1.1 mW/mm^2 stimulation, and -0.24 (p<1e-5) for 458nm 4.3 mW/mm^2 stimulation. We will incorporate an additional analysis to address this issue by identifying responding vessels as those showing supra-threshold percent change in their radius (instead of SD).

Author response image 9.

A plot of the vessel radius change elicited by photostimulation vs. baseline radius standard deviation in vessels with a baseline radius greater than 5 um.

References

(1) Alarcon-Martinez L, Villafranca-Baughman D, Quintero H, et al. Interpericyte tunnelling nanotubes regulate neurovascular coupling. Nature. 2020;kir 2.1(7823):91-95. doi:10.1038/s41586-020-2589-x

(2) Mester JR, Bazzigaluppi P, Weisspapir I, et al. In vivo neurovascular response to focused photoactivation of Channelrhodopsin-2. NeuroImage. 2019;192:135-144. doi:10.1016/j.neuroimage.2019.01.036

(3) O’Herron PJ, Hartmann DA, Xie K, Kara P, Shih AY. 3D optogenetic control of arteriole diameter in vivo. Nelson MT, Calabrese RL, Nelson MT, Devor A, Rungta R, eds. eLife. 2022;11:e72802. doi:10.7554/eLife.72802

(4) Hartmann DA, Berthiaume AA, Grant RI, et al. Brain capillary pericytes exert a substantial but slow influence on blood flow. Nat Neurosci. Published online February 18, 2021:1-13. doi:10.1038/s41593-020-00793-2

(5) Mester JR, Bazzigaluppi P, Dorr A, et al. Attenuation of tonic inhibition prevents chronic neurovascular impairments in a Thy1-ChR2 mouse model of repeated, mild traumatic brain injury. Theranostics. 2021;11(16):7685-7699. doi:10.7150/thno.60190

(6) Mester JR, Rozak MW, Dorr A, Goubran M, Sled JG, Stefanovic B. Network response of brain microvasculature to neuronal stimulation. NeuroImage. 2024;287:120512. doi:10.1016/j.neuroimage.2024.120512

(7) Hall CN, Reynell C, Gesslein B, et al. Capillary pericytes regulate cerebral blood flow in health and disease. Nature. 2014;508(7494):55-60. doi:10.1038/nature13165

Author Response

We thank both the editors and the Reviewers for their thoughtful comments and recommendations, that will certainly help us improve the manuscript. Below we address in a brief format some of the comments made, and then outline the changes to the manuscript that we plan to implement in the revision.

We see three interrelated issues in the comments of the Reviewers:

• the length and complexity of the manuscript;

• the link to previously proposed formalisms;

• the impact of adopting the proposed information-theoretic framework.

With regard to all of these issues, we would first like to highlight that the overall goal of our effort was to integrate con tributions to understanding the mechanisms underlying cognitive control across multiple different disciplines, using the information theoretic framework as a common formalism, while respecting and building on prior efforts as much as possible. Accordingly, we sought to be as explicit as possible about how we bridge from prior work using information theory, as well as neural networks and dynamical systems theory, which contributed to length of the original manuscript. While we continue to consider this an important goal, we will do our best to shorten and clarify the main exposition by reorganizing the manuscript as suggested by Reviewer #1 (i.e., in a way that is similar to what we did in our previous Nature Physics paper on multitasking). Specifically, we will move a substantially greater amount of the bridging material to the Supple mentary Information (SI), including the detailed discussion of the Stroop task, and the description of the link to Koechlin & Summerfield’s [L1] information theory formalism. We will also now include an outline of the full model at the beginning of the manuscript, that includes control and learning, and then more succinctly describe simplifications that focus on specific issues and applications in the remainder of the document.

Along similar lines, we will revise and harmonize our presentation of the formalism and notations, to make these more consistent, clearer and more concise throughout the document. Again, some of the inconsistencies in notation arose from our initial description of previous work, and in particular that of Koechlin & Summerfield[L1] that was an important inspiration for our work but that used slightly different notations. An important motivation for our introduction of new notation was that their formulation focused on the performance of a single task at a time, whereas a primary goal of our work was to extend the information theoretic treatment to simultaneous performance of multiple tasks. That is, in focusing on single tasks, Koechlin & Summerfield could refer to a task simply as a direct association between stimuli and responses, whereas we required a way of being able to refer to sets of tasks performed at once (”multitasks”), which in turn required specification of internal pathways. Moreover, they do not provide a mechanism to compute the conditional information Q(a|s) of a response/action s conditioned to a stimulus s does not provide a way to compute it explicitly. Our formalism instead provides a way to explicitly unpack this expression in terms of the efficacies –automatic (Eq. 5) or controlled (Eq. 15)– which can also account for the competition between different stimuli {s1, s2, . . . sn}. It also describes explicitly the competition between multiple tasks (Eq. 18, and Eq. 25 for multiple layers), because different ways of processing schemes for the same combinations of stimuli/responses can incur different levels of internal dependencies and thus require different control strategies.

To mitigate any confusion over terminology we will, as noted above, move a detailed discussion of Koechlin & Summer- field’s formulation, and how it maps to the one we present, to the SI, while taking care to introduce ours clearly at the beginning of the main document, and use it consistently throughout the remainder of the document. We will also make an important distinction – between informational and cognitive costs – more clearly, that we did not do adequately in the original manuscript.

Finally, to more clearly and concretely convey what we consider to be the most important contributions, we will restrict the number of examples we present to ones that relate most directly to the central points (e.g., the effect and limits of control in the presence of interference, and the differences in control strategy under limited temporal horizons). Accompanying our revision, we will also provide a full point-by-point response to the comments and questions raised by the Reviewers. We summarize some the key points we will address below.

PRELIMINARY REPLY TO THE REPORT OF REVIEWER #1

We want to thank the Reviewer for the time and effort put into reviewing our paper and constructive feedback that was provided. We also thank the Reviewer for recognizing the need for a clear computational account of how ”control” manages conflicts by scheduling tasks to be executed in parallel versus serially, and for the positive evaluation on our “efforts of the authors to give these intuitions a more concrete computational grounding.”. As noted in the general reply above, we regret the lack of clarity in several parts of the manuscript and in our introduction and use of the formalism. We consider the following to be the main points to be addressed:

• the role of task graphs and their mapping to standard neural architectures

• the description of entropy and related information-theoretic concepts;

• confusing choice of symbols in our notation between stimuli/responses and serialization/reconfiguration costs;

• missing definition of response time;

Regarding the first part point, we acknowledge that the network architectures we focus on do not draw direct inspiration from conventional machine learning models. Instead, our approach is rooted in the longstanding tradition of using (often simpler, but also more readily interpretable) neural network models to address human cognitive function and how this may be implemented in the brain [L2]; and, in particular, the mechanisms underlying cognitive control (e.g., [L3, L4]). In this context, we emphasize that, for analytical clarity, we deliberately abstract away from many biological details, in an effort to identify those principles of function that are most relevant to cognitive function. Nevertheless, our network architecture is inspired by two concepts that are central to neurobiological mechanisms of control: inhibition and gain modulation. Specifi- cally, we incorporate mutual inhibition among neural processing units, a feature represented by the parameter β. This aspect of our model is consistent with biologically inspired frameworks of neural processing, such as those discussed by Munakata et al. (2011)[L5], reflecting the competitive dynamics observed in neural circuits. Moreover, we introduce the parameter ν to represent a strictly modulatory form of control, akin to the role of neuromodulators in the brain. This modulatory control adjusts the sensitivity of a node to differences among its inputs (e.g., Servan-Schreiber, Printz, & Cohen, (1990)[L6]; Aston-Jones & Cohen (2005)[L7]). Finally, as the Reviewer notes, additional hidden layers can improve expressivity in neural networks, enabling the efficient implementation of more complex tasks, and are a universal feature of biological and artificial neural systems. We thus examined multitasking capability under the assumption that multiple hidden layers are present in a network; irrespective of whether they are needed to implement the corresponding tasks.

Regarding the second point, as noted above, we believe that the confusion arose from our review of the work by Koechlin & Summerfield. In their formalism, in which an action a is chosen (from a set of potential actions) with probability p(a), the cost of choosing that action is − log p(a). This is usually referred to as the information content or, alternatively, the localized entropy [L8]. As the Reviewer correctly observed, the canonical (Shannon) entropy is actually the expectation lEa[− log p(a)] over the localized entropies of a set of actions. In summarizing their formulation, we misleadingly stated that ”they used standard Shannon entropy formalism as a measure of the information required to select the action a.” We will now correct this to state: “[..] they used local entropy (− log p(a)) as a measure of the information required to select the action a, that can be treated as the cost of choosing that action.” We follow this formulation in our own, referring to informational cost as Ψ, and generalizing this to include cases in which more than one action may be chosen to perform at a time.

Regarding the third point, the confusion is due to our use of the letters S and R for both the stimulus and response units (in Sec. II.B) and then serialization and reconstruction costs (in eqs 31-33). We will fix this by renaming the serialization and reconstruction costs more explicitly as S er and Rec.

Finally, we realized we never explicitly stated the expression of the response time we used, but only pointed to it in the literature. In the manuscript we used the expression given in Eq. 53 of [L9], which provides response times as function of the error rates ER and the number of options .

PRELIMINARY REPLY TO THE REPORT OF REVIEWER #2

We want to thank the Reviewer for recognizing our effort to ”rigorously synthesize ideas about multi-tasking within an information-theoretic framework” and its potential. We also thank the Reviewer for the careful comments.

To our best understanding, and similarly to Reviewer #1, the main comments of the Reviewer are on:

• the length and density of the paper;

• the presentation of the Koechlin & Summerfield’s formalism, and the mismatch/lack of clarity of ours in certain points;

• the added value of the information theoretic formalism.

Regarding the first two points, which are common to Reviewer #1, we plan to move a significant part of the manuscript to the Supplementary Information, both to improve readability and make the manuscript shorter, as well as to provide one consistent and cleaner formalism (in particular with regards to the typos and errors highlighted by the Reviewer). In par- ticular, with respect to the comment on Eq. 4-5-6, we will clarify that the probability p[ fi j] is the probability that a certain input dimension (i in this case) is selected by on node j to produce its response (averaged over the individual inputs in each input dimension). We will also take care to make sure that the definition and domain of the various probabilities and probability distributions we use are clearly delineated (e.g. where the costs computed for tasks and task pathways come from).

Regarding the third point, we hope that our work offers value in at least two ways: i) it helps bring unity to ideas and descriptions about the capacity constraints associated with cognitive control that have previously been articulated in different forms (viz., neural networks, dynamical systems, and statistical mechanical accounts); and ii) doing so within an information theoretic framework not only lends rigor and precision to the formulation, but also allows us to cast the allocation of control in normative form – that is, as an optimization problem in which the agent seeks to minimize costs while maximizing gains. While we do not address specific empirical phenomena or datasets in the present treatment, we have done our best to provide examples showing that: a) our information theoretic formulation aligns with treatments using other formalisms that have been used to address empirical phenomena (e.g., with neural network models of the Stroop task); and b) our formulation can be used as a framework for providing a normative approach to widely studied empirical phenomena (e.g., the transition from control-dependent to automatic processing during skill acquisition) that, to date, have been addressed largely from a descriptive perspective; and that it can provide a formally rigorous approach to addressing such phenomena.

[L1] E. Koechlin and C. Summerfield, Trends in cognitive sciences 11, 229 (2007).

[L2] J. L. McClelland, D. E. Rumelhart, P. R. Group, et al., Explorations in the Microstructure of Cognition 2, 216 (1986).

[L3] J. D. Cohen, K. Dunbar, and J. L. McClelland, Psychological Review 97, 332 (1990).

[L4] E. K. Miller and J. D. Cohen, Annual review of neuroscience 24, 167 (2001).

[L5] Y. Munakata, S. A. Herd, C. H. Chatham, B. E. Depue, M. T. Banich, and R. C. O’Reilly, Trends in cognitive sciences 15, 453 (2011).

[L6] D. Servan-Schreiber, H. Printz, and J. D. Cohen, Science 249, 892 (1990).

[L7] G. Aston-Jones and J. D. Cohen, Annu. Rev. Neurosci. 28, 403 (2005).

[L8] T. F. Varley, Plos one 19, e0297128 (2024).

[L9] T. McMillen and P. Holmes, Journal of Mathematical Psychology 50, 30 (2006).

Author response:

We deeply appreciate the editors’ and reviewers’ invaluable time and effort. We would also like to extend our gratitude to eLife for its unwavering commitment to a transparent review and publication model. Below, we present our point-by-point responses to the comments.  

Besides the WT allele, equivalent to the mouse TMEM173 gene, the human TMEM173 gene has two common alleles: the HAQ and AQ alleles carried by billions of people. The main conclusions and interpretation, summarized in the Title and Abstract, are (i) Different from the WT TMEM173 allele, the HAQ or AQ alleles are resistant to STING activation-induced cell death; (ii) STING residue 293 is critical for cell death; (iii) HAQ, AQ alleles are dominant to the SAVI allele; iv) One copy of the AQ allele rescues the SAVI disease in mice. We propose that STING research and STING-targeting immunotherapy should consider human TMEM173 heterogeneity. These interpretations and conclusions were based on Data and Logic. We welcome alternative, logical interpretations from our peers and potential collaborations to advance the human TMEM173 research.  

Reviewer #1 (Public Review):

Responses to Comment 1: We greatly appreciate Reviewer 1's insights. We will change the “lymphocytes” to “splenocytes” (line 134) as suggested. We respectfully disagree with Reviewer 1’s comments on TBK1 (lines 129 – 134). First, we used two different TBK1 inhibitors: BX795 and GSK8612. Second, because BX795 also inhibits PDK1, we used a PDK1 inhibitor GSK2334470; Third, both BX795 and GSK8612 completely inhibited diABZI-induced splenocyte cell death (Figure 1B). The logical conclusion is “TBK1 activation is required for STING-mediated mouse spleen cell death ex vivo”. (line 118). 

This manuscript uncovers a significant aspect of the interplay between the common human TMEM173 alleles and the rare SAVI mutation (lines 23-26). Our discovery that the common human TMEM173 alleles are resistant to STING activation-induced cell death is a substantial finding. It further strengthens the argument that the HAQ and AQ alleles are functionally distinct from the WT allele 1-3. We wish to underscore the crucial message of this study-that 'STING research and STING-targeting immunotherapy should consider TMEM173 heterogeneity in humans' (line 37), which has been largely overlooked in current STING clinical trials 4.  

Regarding STING-Cell death, as we stated in the Introduction (lines 62-79). (i) STING-mediated cell death is cell type-dependent 5-7 and type I IFNs-independent 5,7,8. (ii) The in vivo biological significance of STING-mediated cell death is not clear 7,8. (iii) The mechanisms of STING-Cell death remain controversial. Multiple cell death pathways, i.e., apoptosis, necroptosis, pyroptosis, ferroptosis, and PANoptosis, are proposed 7,9,10. SAVI patients (WT/SAVI) and mouse models had CD4 T cellpenia 8,11. SAVI/HAQ, SAVI/AQ restored T cells in mice. Thus, the manuscript provides some answers to the biological significance of STING-cell death. Next, splenocytes from Q293/Q293 mice are resistant to STING cell death. The logical conclusion is that the amino acid 293 is critical for STING cell death. How aa293 mediates this function needs future investigation. Similarly, how TBK1 mediates STING cell death, independent of type I IFNs and NFκB induction, needs future investigation.

Responses to Comment 2: These are all very interesting questions that we will address in future studies. This manuscript, titled “The common TMEM173 HAQ, AQ alleles rescue CD4 T cellpenia, restore T-regs, and prevent SAVI (N153S) inflammatory disease in mice” does not focus on Q293 mice. We have been researching the common human TMEM173 alleles since 2011 from the discovery12 , mouse model1,3, human clinical trial2, and human genetics studies 3. This manuscript is another step towards understanding these common human TMEM173 alleles with the new discovery that HAQ, AQ are resistant to STING cell death. 

Responses to Comment 3: We aim to address these worthy questions in future studies. In this manuscript, Figure 6 shows AQ/SAVI had more T-regs than HAQ/SAVI (lines 246 – 256). In our previous publication on HAQ, AQ knockin mice, we showed that AQ T-regs have more IL-10 and mitochondria activity than HAQ T-regs 3. We propose that increased IL-10+

Tregs in AQ mice may contribute to an improved phenotype in AQ/SAVI compared to

HAQ/SAVI. However, we are not excluding other contributions (e.g. metabolic difference) by the AQ allele. We will explore these possibilities in future research.   

Responses to Comment 4: Figure 2 is necessary because it reveals the difference between mouse and human STING cell death. Figure 2A-2B showed that STING activation killed human CD4 T cells, but not human CD8 T cells or B cells. This observation is different from Figure 1A, where STING activation killed mouse CD4, CD8 T cells, and CD19 B cells, revealing the species-specific STING cell death responses. Regarding human CD8 T cells, as we stated in the Discussion (lines 318-320), human CD8 T cells (PBMC) are not as susceptible as the CD4 T cells to STING-induced cell death 8. We used lung lymphocytes that showed similar observations (Figure 2A). For Figure 2C, we used 2 WT/HAQ and 3 WT/WT individuals (lines 738-739). We generate HAQ, AQ THP-1 cells in STING-KO THP-1 cells (Invivogen,, cat no. thpd-kostg) (lines 740-741). 

A recent study found that STING agonist SHR1032 induces cell death in STING-KO THP-1 cells expressing WT(R232) human STING 10 (line 182) independent of type I IFNs. SHR1032 suppressed THP1-STING-WT(R232) cell growth at GI50: 23 nM while in the parental THP1STING-HAQ cells, the GI50 of SHR1032 was >103 nM 10. Cytarabine was used as an internal control where SHR1032 killed more robustly than cytarabine in the THP1-STING-WT(R232) cells but much less efficiently than cytarabine in the THP-1-STING-HAQ cells 10.   

This manuscript rigorously uses mouse splenocytes, human lung lymphocytes, THP-1 reconstituted with HAQ, AQ, and HAQ/SAVI, AQ/SAVI mice, to demonstrate that the common human HAQ, AQ alleles are resistant to STING cell death in vitro and in vivo.

We agree with reviewer 1 that STING-mediated cell death mechanisms in myeloid and lymphoid cells may be different and likely contribute to the different mechanisms proposed in STING cell death research 7,9,10. Our study focuses on the in vivo mechanism of T cellpenia.  

Responses to Comment 5: We stated in the Introduction that “AQ responds to CDNs and produce type I IFNs in vivo and in vitro 3,13,14 ”(line 94, 95). We reported that the AQ knock in mice responded to STING activation 3. We previously showed that there was a negative natural selection on the AQ allele in individuals outside of Africa 3. 28% of Africans are WT/AQ but only 0.6% East Asians are WT/AQ 3. Future research on the AQ allele will address this interesting question that may shed new mechanistic light on STING action.

Responses to Comment 6: The comment here is similar to comment 3. In this manuscript, Figure 6 shows AQ/SAVI had more T-regs than HAQ/SAVI (lines 246 – 256). In our previous publication on HAQ, AQ knockin mice, we showed that AQ T-regs have more IL-10 and mitochondria activity than HAQ T-regs 3. We propose that increased IL-10+ Tregs in AQ mice may contribute to an improved phenotype in AQ/SAVI compared to HAQ/SAVI. However, we are not excluding other contributions (e.g. metabolic difference) by the AQ allele.

Responses to Comment 7: Both radioresistant parenchymal and/or stromal cells and hematopoietic cells influence SAVI pathology in mice 15,16. Nevertheless, the lack of CD 4 T cells, including the anti-inflammatory T-regs, likely contributes to the inflammation in SAVI mice and patients. We characterized lung function, lung inflammation (Figure 4), lung neutrophils, and inflammatory monocyte infiltration (Figure S4). 

Responses to Comment 8: Several publications have linked STING to HIV pathogenesis 17-22  (line 271). The manuscript studies STING activation-induced cell death. It is not stretching to ask, for example, does preventing STING cell death, without affecting type I IFNs production, restore CD4 T cell counts and improve care for AIDS patients?

Reviewer #2 (Public Review):

Response to Comment 1: Please see the Figure below for cell death by diABZI, DMXAA in Splenocytes from WT/WT, WT/HAQ, HAQ/SAVI, AQ/SAVI mice. The HAQ/SAVI and AQ/SAVI splenocytes showed similar partial resistance to STING activationinduced cell death. 

Responses to Comment 2: We examined HAQ, AQ mouse splenocytes, HAQ human lung lymphocytes, THP-1 reconstituted with HAQ, AQ, and HAQ/SAVI, AQ/SAVI mice, to demonstrate that the common human HAQ, AQ alleles are resistant to STING cell death in vitro and in vivo. Additional human T cell line work does not add too much. 

Responses to Comment 3: This is possibly a misunderstanding. We use BMDM for the purpose of comparing STING signaling (TBK1, IRF3, NFκB, STING activation) by WT/SAVI, HAQ/SAVI, AQ/SAVI. Ideally, we would like to compare STING signaling in CD4 T cells from WT/SAVI to HAQ/SAVI, AQ/SAVI mice. However, WT/SAVI has no CD4 T cells. Here, we are making the assumption that the basic STING signaling (TBK1, IRF3, NFκB, STING activation) is conserved between T cells and macrophages. 

Responses to Comment 4: Reviewer 2 suggests looking for evidence of inflammation and STING activation in the lungs of HAQ/SAVI, AQ/SAVI. We would like to elaborate further. First, anti-inflammatory treatments, e.g. steroids, DMARDs, IVIG, Etanercept, rituximab, Nifedipine, amlodipine, et al., all failed in SAVI patients 11. Second, Figure S4 examined lung neutrophils and inflammatory monocyte infiltration. Interestingly, while AQ/SAVI mice had a better lung function than HAQ/SAVI mice (Figure 4D, 4E vs 4H, 4I), HAQ/SAVI and AQ/SAVI lungs had comparable neutrophils and inflammatory monocyte infiltration. Last, SAVI is classified as type I interferonopathy 11, but the lung diseases of SAVI are mainly independent of type I IFNs 23-26. The AQ allele suppresses SAVI in vivo.  Understanding the mechanisms by which AQ rescues SAVI can generate curative care for SAVI patients.  

Author response image 1.

(A-B). Flow cytometry of HAQ/SAVI, AQ/SAVI, WT/WT or WT/HAQ splenocytes treated with diABZI (100ng/ml) or DMXAA (20µg/ml) for 24hrs. Cell death was determined by PI staining. Data are representative of three independent experiments. Graphs represent the mean with error bars indication s.e.m. p values are determined by one-way ANOVA Tukey’s multiple comparison test. * p<0.05. n.s: not significant.

References.

(1)             Patel, S. et al. The Common R71H-G230A-R293Q Human TMEM173 Is a Null Allele. J Immunol 198, 776-787 (2017). 

(2)             Sebastian, M. et al. Obesity and STING1 genotype associate with 23-valent pneumococcal vaccination efficacy. JCI Insight 5 (2020). 

(3)             Mansouri, S. et al. MPYS Modulates Fatty Acid Metabolism and Immune Tolerance at Homeostasis Independent of Type I IFNs. J Immunol 209, 2114-2132 (2022). 

(4)             Sivick, K. E. et al. Comment on "The Common R71H-G230A-R293Q Human TMEM173 Is a Null Allele". J Immunol 198, 4183-4185 (2017). 

(5)             Gulen, M. F. et al. Signalling strength determines proapoptotic functions of STING. Nat Commun 8, 427 (2017). 

(6)             Kabelitz, D. et al. Signal strength of STING activation determines cytokine plasticity and cell death in human monocytes. Sci Rep 12, 17827 (2022). 

(7)             Murthy, A. M. V., Robinson, N. & Kumar, S. Crosstalk between cGAS-STING signaling and cell death. Cell Death Differ 27, 2989-3003 (2020). 

(8)             Kuhl, N. et al. STING agonism turns human T cells into interferon-producing cells but impedes their functionality. EMBO Rep 24, e55536 (2023). 

(9)             Li, C., Liu, J., Hou, W., Kang, R. & Tang, D. STING1 Promotes Ferroptosis Through MFN1/2-Dependent Mitochondrial Fusion. Front Cell Dev Biol 9, 698679 (2021). 

(10)         Song, C. et al. SHR1032, a novel STING agonist, stimulates anti-tumor immunity and directly induces AML apoptosis. Sci Rep 12, 8579 (2022). 

(11)         Liu, Y. et al. Activated STING in a vascular and pulmonary syndrome. N Engl J Med 371, 507-518 (2014). 

(12)         Jin, L. et al. Identification and characterization of a loss-of-function human MPYS variant. Genes Immun 12, 263-269 (2011). 

(13)         Yi, G. et al. Single nucleotide polymorphisms of human STING can affect innate immune response to cyclic dinucleotides. PLoS One 8, e77846 (2013). 

(14)         Patel, S. et al. Response to Comment on "The Common R71H-G230A-R293Q Human TMEM173 Is a Null Allele". J Immunol 198, 4185-4188 (2017). 

(15)         Gao, K. M. et al. Endothelial cell expression of a STING gain-of-function mutation initiates pulmonary lymphocytic infiltration. Cell Rep 43, 114114 (2024). 

(16)         Gao, K. M., Motwani, M., Tedder, T., Marshak-Rothstein, A. & Fitzgerald, K. A. Radioresistant cells initiate lymphocyte-dependent lung inflammation and IFNgammadependent mortality in STING gain-of-function mice. Proc Natl Acad Sci U S A 119, e2202327119 (2022). 

(17)         Monroe, K. M. et al. IFI16 DNA sensor is required for death of lymphoid CD4 T cells abortively infected with HIV. Science 343, 428-432 (2014). 

(18)         Doitsh, G. et al. Cell death by pyroptosis drives CD4 T-cell depletion in HIV-1 infection. Nature 505, 509-514 (2014). 

(19)         Jakobsen, M. R., Olagnier, D. & Hiscott, J. Innate immune sensing of HIV-1 infection. Curr Opin HIV AIDS 10, 96-102 (2015). 

(20)         Silvin, A. & Manel, N. Innate immune sensing of HIV infection. Curr Opin Immunol 32, 54-60 (2015). 

(21)         Altfeld, M. & Gale, M., Jr. Innate immunity against HIV-1 infection. Nat Immunol 16, 554-562 (2015). 

(22)         Krapp, C., Jonsson, K. & Jakobsen, M. R. STING dependent sensing - Does HIV actually care? Cytokine Growth Factor Rev 40, 68-76 (2018). 

(23)         Luksch, H. et al. STING-associated lung disease in mice relies on T cells but not type I interferon. J Allergy Clin Immunol 144, 254-266 e258 (2019). 

(24)         Stinson, W. A. et al. The IFN-gamma receptor promotes immune dysregulation and disease in STING gain-of-function mice. JCI Insight 7 (2022). 

(25)         Warner, J. D. et al. STING-associated vasculopathy develops independently of IRF3 in mice. J Exp Med 214, 3279-3292 (2017). 

(26)         Fremond, M. L. et al. Overview of STING-Associated Vasculopathy with Onset in Infancy (SAVI) Among 21 Patients. J Allergy Clin Immunol Pract 9, 803-818 e811 (2021).

Author response:

eLife Assessment

This useful study integrates experimental methods from materials science with psychophysical methods to investigate how frictional stabilities influence tactile surface discrimination. The authors argue that force fluctuations arising from transitions between frictional sliding conditions facilitate the discrimination of surfaces with similar friction coefficients. However, the reliance on friction data obtained from an artificial finger, together with the ambiguous correlative analyses relating these measurements to human psychophysics, renders the findings incomplete.

Our main goal with this paper was to show that the most common metric, i.e. average friction coefficient—widely used in tactile perception and device design—is fundamentally unsound, and to offer a secondary parameter that is compatible with the fact that human motion is unconstrained, leading to dynamic interfacial mechanics. In contrast with the summary assessment, we also note that the average friction coefficients in our study were not particularly similar, ranging from differences of 0.4 – 1, a typical range seen in most studies. We believe some of the comments originate from a misinterpretation of our statistically significant, but negative correlation between human results and friction coefficients – which leads to the spurious conclusion that nearly identical objects should be very easy to tell apart, thus supporting our central argument for the need of an alternative. We understand the Reviewers wanting to see that we can demonstrate that humans using instabilities in situ. This is seemingly reasonable, but we explain the significant challenges and fundamental unknowns to those experiments. However, we modified our title to reflect our focus on offering an alternative to the average coefficient of friction.

We do not think it was feasible, at this stage, to demonstrate that humans use friction instabilities through direct manipulation and observation in human participants. In short, there are still several fundamental unknowns: (1) a decision-making model would need to be created, but it is unknown if tactile decision making follows other models, (2) it is further unknown what constitutes “tactile evidence”, though at our manuscript’s conclusion, we propose that friction instabilities are better suited for to be tactile evidence than the averaging of friction coefficients from a narrow range of human exploration (3) in the design of samples, from a friction mechanics and materials perspective, it is not at this point, possible to pre-program surfaces a priori to deliver friction instabilities and instead must be experimentally determined – especially when attempting to achieve this in controlled surfaces that do not create other overriding tactile cues, like macroscopic bumps or large differences in surface roughness. (4) Given that the basis for tactile percepts, like which object feels “rougher” or “smoother” is not sufficiently established and we have seen leads to confusion, it is necessary to use a 3-alternative forced choice task which avoids asking objects along a preset perceptual dimension – a challenge recognized by Reviewer 3. However, this would bring in issues of memory in the decision-making model. (5) The prior points are compounded by the fact that, we believe, tactile exploration must be performed in an unconstrained manner, i.e., without an apparatus generating motion onto a stationary finger. Work by Liu et al. (IEEE ToH, 2024) showed that recreating friction obtained during free exploration onto a stationary finger was uninterpretable by the participants, hinting at the importance of efference copies(1). We believe that each of the above-mentioned issues constitutes a significant advance in knowledge and would require discussion and dissemination with the community. Finally, one of our overarching goals is to create a consistent method to characterize surfaces, and given individual variability in human fingers and motion, a machine-based method that can rapidly, consistently, and sufficiently replicate tactile exploration is needed.

Finally, we also justify our use of a mock finger to provide a method to characterize surfaces in tactile studies that other researchers could reasonably recreate, without creating a standard around individual humans, considering the variability in finger shape and motion during exploration. We do not believe this is an “either-or” argument, but rather that standardized methods to characterize surfaces and devices are greatly needed in the field. From these standardized methods, like surface roughness, some tabulated values of friction coefficient, or surface energy, etc., the current metrics to parameterize results are largely incapable of capturing the dynamic changes in forces expected during human tactile exploration.

Our changes to the manuscript (Page 1 & SI Page 1, Title)

“Alternatives to Friction Coefficient: Role of Frictional Instabilities for Fine Touch Perception”

Reviewer 1 (Public review):

Summary:

In this paper, Derkaloustian et. al look at the important topic of what affects fine touch perception. The observations that there may be some level of correlation with instabilities are intriguing. They attempted to characterize different materials by counting the frequency (occurrence #, not of vibration) of instabilities at various speeds and forces of a PDMS slab pulled lengthwise over the material. They then had humans make the same vertical motion to discriminate between these samples. They correlated the % correct in discrimination with differences in frequency of steady sliding over the design space as well as other traditional parameters such as friction coefficient and roughness. The authors pose an interesting hypothesis and make an interesting observation about the occurrences of instability regimes in different materials while in contact with PDMS, which is interesting for the community to see in the publication. It should be noted that the finger is complex, however, and there are many factors that may be quite oversimplified with the use of the PDMS finger, and the consideration and discounting of other parameters are not fully discussed in the main text or SI. Most importantly, however, the conclusions as stated do not align with the primary summary of the data in Figure 2.

Strengths:

The strength of this paper is in its intriguing hypothesis and important observation that instabilities may contribute to what humans are detecting as differences in these apparently similar samples.

We thank Reviewer 1 for their time on the manuscript, recognizing the approach we took, and offering constructive feedback. We believe that our conclusions, in fact, are supported by the primary summary of the data in Figure 2 but we believe that our use of R² could have led to misinterpretation. The trend with friction coefficient and percent correct was indeed statistically significant but was spurious because the slope was negative. In the revision, we add clarifying comments throughout, change from R² to r as to highlight the negative trend, and adjust the figures to better focus on friction coefficient.

Finally, we added a new section to discuss the tradeoffs between using a real human finger versus a mock finger, and which situations may warrant the use of one or the other. In short, for our goal of characterizing surfaces to be used in tactile experiments, we believe a mock finger is more sustainable and practical than using real humans because human fingers are unique per participant, humans move their fingers at constantly changing pressures and velocities, and friction generated during free exploring human cannot be satisfactorily replicated by moving a sample onto a stationary finger. But, we do not disagree that for other types of experiments, characterizing a human participant directly may be more advantageous.

Weaknesses:

Comment 1 - The most important weakness is that the findings do not support the statements of findings made in the abstract. Of specific note in this regard is the primary correlation in Figure 2B between SS (steady sliding) and percent correct discrimination. Of specific note in this regard is the primary correlation in Figure 2B between SS (steady sliding) and percent correct discrimination. While the statistical test shows significance (and is interesting!), the R-squared value is 0.38, while the R-squared value for the "Friction Coefficient vs. Percent Correct" plot has an R-squared of 0.6 and a p-value of < 0.01 (including Figure 2B). This suggests that the results do not support the claim in the abstract: "We found that participant accuracy in tactile discrimination was most strongly correlated with formations of steady sliding, and response times were negatively correlated with stiction spikes. Conversely, traditional metrics like surface roughness or average friction coefficient did not predict tactile discriminability."

We disagree that the trend with friction coefficient suggests the results do not support the claim because the correlation was found to be negative. However, we could have made the comparison more apparent and expanded on this point, given its novelty.

While the R² value corresponding to the “Friction Coefficient vs. Percent Correct” plot is notably higher, our results show that the slope is negative, which would be statistically spurious. This is because a negative correlation between percent correct (accuracy in discriminating surfaces) and difference in friction coefficient means that the more similar two surfaces are (by friction coefficient), the easier it would be for people to tell them apart. That is, it incorrectly concludes that two identical surfaces would be much easier to tell apart than two surfaces with greatly different friction coefficients.

This is counterintuitive to nearly all existing results, but we believe our samples were well-positioned to uncover this trend by minimizing variability, by controlling multiple physical parameters in the samples, and that the friction coefficient — typically calculated in the field as an average friction coefficient — ignores all the dynamic changes in forces present in elastic systems undergoing mesoscale friction, i.e., human touch, as seen in Fig. 1 in a mock finger and Fig. 3 in a real finger. By demonstrating this statistically spurious trend, we believe this strongly supports our premise that an alternative to friction coefficient is needed in the design of tactile psychophysics and haptic interfaces.

We believe that this could have been misinterpreted, so we took several steps to improve clarity, given the importance of this finding: we separated the panel on friction coefficient to its own panel, we changed from R² to r throughout, and we added clarifying text. We also added a small section focusing on this spurious trend.

Our changes to the manuscript (Page 10)

“To compare the value of looking at frictional instabilities, we also performed GLMM fits on common approaches in the field, like a friction coefficient or material property typically used in tactile discrimination, shown in Fig. 2D-E. Interestingly, in Fig. 2D, we observed a spurious, negative correlation between friction coefficient (typically and often problematically simplified as across all tested conditions) and accuracy (r = -0.64, p < 0.01); that is, the more different the surfaces are by friction coefficient, the less people can tell them apart. This spurious correlation would be the opposite of intuition, and further calls into question the common practice of using friction coefficients in touch-related studies. The alternative, two-term model which includes adhesive contact area for friction coefficient(29) was even less predictive (see Fig. S6A of SI). We believe such a correlation could not have been uncovered previously as our samples are minimal in their physical variations. Yet, the dynamic changes in force even within a single sample are not considered, despite being a key feature of mesoscale friction during human touch.

We investigate different material properties in Fig. 2E. Differences in average roughness R_a (or other parameters, like root mean square roughness R_rms (Fig. S6A of SI) did not show a statistically significant correlation to accuracy. Though roughness is a popular parameter, correlating any roughness parameter to human performance here could be moot: the limit of detecting roughness differences has previously been defined as 13 nm on structured surfaces33 and much higher for randomly rough surfaces,(46) all of which are magnitudes larger than the roughness differences between our surfaces. The differences in contact angle hysteresis – as an approximation of the adhesion contributions(47) – do not present any statistically significant effects on performance.”

Comment 2, Part 1

Along the same lines, other parameters that were considered such as the "Percent Correct vs. Difference in Sp" and "Percent Correct vs. Difference in SFW" were not plotted for consideration in the SI. It would be helpful to compare these results with the other three metrics in order to fully understand the relationships.

We have added these plots to the SI. We note that we had checked these relationships and discussed them briefly, but did not include the plot. The plots show that the type of instability was not as helpful as its presence or absence.

Our changes to the manuscript (Page 9)

“Furthermore, a model accounting for slow frictional waves alone specifically shows a significant, negative effect on performance (p < 0.01, Fig. S5 of SI), suggesting that in these samples and task, the type of instability was not as important.”

Added (SI Page 4)

“and no correlation between accuracy and stiction spikes (Fig. S5).”

Comment 2, Part 2

Other parameters such as stiction magnitude and differences in friction coefficient over the test space could also be important and interesting.

We agree these are interesting and have thought about them. We are aware that others, like Gueorguiev et al., have studied stiction magnitudes, and though there was a correlation, the physical differences in surface roughness (glass versus PMMA) investigated made it unclear if these could be generalized further(2). We are unsure how to proceed here with a satisfactory analysis of stiction magnitude, given that stiction spikes are not always generated. In fact, Fig. 1 shows that for many velocities and pressures, they do not form. However, we offer some speculation on why stiction spikes may be overrepresented in the literature because:

(1) They are prone to being created if the finger was loaded for a long time onto a surface prior to movement, thus creating adhesion by contact aging which is unlike active human exploration. We avoid this by discarding the first pull in our measurements, and is a standard practice in mechanical characterization if contact aging needs to be avoided.

(2) The ranges of velocities and pressures explored were small.

(3) In an effort to generate strong tactile stimuli, highly adhesive or rough surfaces are used.

(4) They are visually distinctive on a plot, but we are unaware of any mechanistic reason that mechanoreceptors would be extremely sensitive to this low frequency event over other signals.

In ongoing work, however, we are always cognizant that if stiction spikes are a dominant factor, then a secondary analysis on their magnitude would be important.

We interpret “difference in friction coefficient over the test space” to be, for a single surface, like C4, to find the highest average friction for a condition of single velocity and mass and subtract that from the lowest average friction for a condition of single velocity and mass. We calculated the difference in friction coefficient in the typical manner of the field, by averaging all data collected at all velocities and masses and assigning a single value for all of a surface, like C4. We had performed this, and have the data, but we are wary of overinterpreting secondary and tertiary metrics because they do not have any fundamental basis in traditional tribology, and this value, if used by humans, would suggest that they rapidly explore a large parameter space to find a “maximum” and “minimum” friction. Furthermore, the range in friction across the test space, after averaging, may in fact, be smaller than the range of friction in a single measurement. For example, in Fig. 1B, the friction coefficient can be calculated by dividing the data by the normal force ([applied mass + 6 g finger] × gravity). The friction coefficient in a single run varies widely, as expected.

Fig. 2D shows a GLMM fit between percent correct responses across our pairs and the differences in friction coefficient for each pair, where we see a spurious negative correlation. As we had the data of all average friction coefficients for each condition for a given material, we also looked at the difference in maximum and minimum friction coefficients. For our tested pairs, these differences also lined up on a statistically significant, negative GLMM fit (r = -0.86, p < 0.005). However, the values for a given surface can vary drastically, with an interquartile range of 1.20 to 2.09 on a single surface. We fit participant accuracy to the differences in these IQRs across pairs. This also led to a negative GLMM fit (r = -0.65, p < 0.05). However, we are hesitant to add this to the manuscript for the reasons stated previously.

Comment 3, Part 1

Beyond this fundamental concern, there is a weakness in the representativeness of the PDMS finger, the vertical motion, and the speed of sliding to real human exploration.

Overall, this is a continuous debate that we think offers two solutions. There is always a tradeoff between using a synthetic model of a finger versus a real human finger, and there is a place for both models. That is, while our mock finger will be more successful the closer it is to a human finger, it is not our goal to fully replace a human finger, rather our goal is to provide a method of characterizing surfaces that is indeed relevant on the length scale of human touch.

The usefulness of the mock finger is in isolating the features of each surface that is independent of human variability, i.e., instabilities that form without changing loading conditions between sliding motions or even within one sliding motion. Of course, with this method, we still require confirmation of these features still forming during human exploration, which we show in Fig. 3.

We believe that this method of characterizing surfaces at the mesoscale will ultimately lead to more successful human studies on tactile perception. Currently, and as shown in the paper, characterizing surfaces through traditional techniques, such as a commercial tribometer (friction coefficient, using a steel or hard metal ball), roughness (via atomic force microscopy or some other metrology), surface energy are less predictive. Thus, we believe this mock finger is stronger than the current state-of-the-art characterizing surfaces (we are also aware of a commercial mock finger company, but we were unable to purchase or obtain an evaluation model).

One of the main – and severe – limitations of using a human finger is that all fingers are different, meaning any study focusing on a particular user may not apply to others or be recreated easily by other researchers. We cannot set a standard for replication around a real human finger as that participant may no longer be available, or willing to travel the world as a “standard”. Furthermore, the method in which changes their pressures and velocities is different. We note that this is a challenge unique to touch perception – how an object is touched changes the friction generated, and thus the tactile stimulus generated, whereas a standardized stimulus is more straightforward for light or sound.

However, we do emphasize that we have strongly considered the balance between feasibility and ecological validity in the design of a mock finger. We have a mock finger, with the three components of stiffness of a human finger (more below). Furthermore, we have also successfully used this mock finger in correlations with human psychophysics in previous work, where findings from our mechanical experiments were predictive of human performance(3-6).

Our changes to the manuscript Added (Page 2-3)

“Mock finger as a characterization tool

In this work, we use a mechanical setup with a PDMS mock finger to derive tactile predictors from controlled friction traces alternative to average friction coefficients. While there is a tradeoff in selecting a synthetic finger over a more accurate, real human finger in modeling touch, our aim to design a method of mesoscale surface characterization for more successful studies on tactile perception cannot be fulfilled using one human participant as a standard. We believe that with sufficient replication of surface and bulk properties as well as contact geometry, and controlled friction measurements collected at loading conditions observed during a tactile discrimination task, we can isolate unique frictional features of a set of surfaces that do not arise from human-to-human variability.

The major component of a human finger, by volume, is soft tissue (~56%)(22), resulting in an effective modulus close to 100 kPa(23,24). In order to achieve this same softness, we crosslink PDMS in a 1×1×5 cm mold at a 30:1 elastomer:crosslinker ratio. However, two more features impart increased stiffness in a human finger. Most of this added rigidity is derived from the bone at the fingertip, the distal phalanx(23–25), which we mimic with an acrylic bone within our PDMS network. The stratum corneum, the stiffer, glassier outer layer of skin(26), is replicated with the surface of the mock finger glassified, or further crosslinked, after 8 hours of UV-Ozone treatment(27). This treatment also modifies the surface properties of the native PDMS to align with those of a human finger more closely. It minimizes the viscoelastic tack at the surface, resulting in a comparable non-sticky surface. At least one day after treatment, the finger surface returns to moderate hydrophilicity (~60º), as is typically observed for a real finger(28).

The initial contact area formed before a friction trace is collected is a rectangle of 1×1 cm. While this shape is not entirely representative of a human finger with curves and ridges, human fingers flatten out enough to reduce the effects of curvature with even very light pressures(28–30). This implies that regardless of finger pressure, the contact area is largely load-independent, which is more accurately replicated with a rectangular mock finger. It is still a challenge to control pressure distribution with this planar interface, but non-uniform pressures are also expected during human exploration.

Lastly, we consider fingerprints vs. flat fingers. A key finding of our previous work is that while fingerprints enhanced frictional dynamics at certain conditions, key features were still maintained with a flat finger.7 Furthermore, for some loading conditions, the more amplified signals could also result in more similar friction traces for different surfaces. We have continued to use flat fingers in our mechanical experiments, and have observed good agreement between these friction traces and human experiments(7,8,21,31).”

(Page 3-4, Materials and Methods)

“Mock Finger Preparation

Friction forces across all six surfaces were measured using a custom apparatus with a polydimethylsiloxane (PDMS, Dow Sylgard 184) mock finger that mimics a human finger’s

mechanical properties and contact mechanics while exploring a surface relatively closely(7,8). PDMS and crosslinker were combined in a 30:1 ratio to achieve a stiffness of 100 kPa comparable to a real finger, then degassed in a vacuum desiccator for 30 minutes. We are aware that the manufacturer recommended crosslinking ratio for Sylgard 184 is 10:1 due to potential uncrosslinked liquid residues(32), but further crosslinking concentrated at the surface prevents this. The prepared PDMS was then poured into a 1×1×5 cm mold also containing an acrylic 3D-printed “bone” to attach applied masses on top of the “fingertip” area contacting a surface during friction testing. After crosslinking in the mold at 60ºC for 1 hour, the finger was treated with UV-Ozone for 8 hours out of the mold to minimize viscoelastic tack.

Mechanical Testing

A custom device using our PDMS mock finger was used to collect macroscopic friction force traces replicating human exploration(7,8). After placing a sample surface on a stage, the finger was lowered at a slight angle such that an initial 1×1 cm rectangle of “fingertip” contact area could be established. We considered a broad range of applied masses (M \= 0, 25, 75, and 100 g) added onto the deadweight of the finger (6 g) observed during a tactile discrimination task. The other side of the sensor was connected to a motorized stage (V-508 PIMag Precision Linear Stage, Physikinstrumente) to control both displacement (4 mm across all conditions) and sliding velocity (v \= 5, 10, 25, and 45 mm s^-1). Forces were measured at all 16 combinations of mass and velocity via a 250 g Futek force sensor (k \= 13.9 kN m^-1) threaded to the bone, and recorded at an average sampling rate of 550 Hz with a Keithley 7510 DMM digitized multimeter. Force traces were collected in sets of 4 slides, discarding the first due to contact aging. Because some mass-velocity combinations were near the boundaries of instability phase transitions, not all force traces at these given conditions exhibited similar profiles.

Thus, three sets were collected on fresh spots for each condition to observe enough occurrences of multiple instabilities, at a total of nine traces per combination for each surface.”

Added References (Page 13)

M. Murai, H.-K. Lau, B. P. Pereira and R. W. H. Pho, J. Hand Surg., 1997, 22, 935–941.

A. Abdouni, M. Djaghloul, C. Thieulin, R. Vargiolu, C. Pailler-Mattei and H. Zahouani, R. Soc. Open Sci., DOI:10.1098/rsos.170321.

P.-H. Cornuault, L. Carpentier, M.-A. Bueno, J.-M. Cote and G. Monteil, J. R. Soc. Interface, DOI:10.1098/rsif.2015.0495.

K. Qian, K. Traylor, S. W. Lee, B. Ellis, J. Weiss and D. Kamper, J. Biomech., 2014, 47, 3094– 3099.

Y. Yuan and R. Verma, Colloids Surf. B Biointerfaces, 2006, 48, 6–12.

Y.-J. Fu, H. Qui, K.-S. Liao, S. J. Lue, C.-C. Hu, K.-R. Lee and J.-Y. Lai, Langmuir, 2010, 26, 4392–4399.

Comment 3, Part 2

“The real finger has multiple layers with different moduli. In fact, the stratum corneum cells, which are the outer layer at the interface and determine the friction, have a much higher modulus than PDMS. The real finger has multiple layers with different moduli. In fact, the stratum corneum cells, which are the outer layer at the interface and determine the friction, have a much higher modulus than PDMS.

We have approximated the softness of the finger with 100 kPa crosslinked PDMS, which is close to what has been reported for the bulk of a human fingertip(8,9). However, as mentioned in the Materials and Methods, there are two additional features of the mock finger that impart greater strength. The PDMS surrounds a rigid, acrylic bone comparable to the distal phalanx, which provides an additional layer of higher modulus(10). Additionally, the 8-hour UV-Ozone treatment decreases the viscoelastic tack of the pristine PDMS by glassifying, or further crosslinking the surface of the finger(11), therefore imparting greater stiffness at the surface similar to the contributions of the stratum corneum, along with a similar surface energy(12). This technique is widely used in wearables(13), soft robotics(14), and microfluidics(15) to induce both these material changes. Additionally, the finger is used at least a day after UV-Ozone treatment is completed in order for the surface to return to moderate hydrophilicity, similar to the outermost layer of human skin(16).

Comment 3, Part 3

In addition, the slanted position of the finger can cause non-uniform pressures across the finger. Both can contribute to making the PDMS finger have much more stick-slip than a real finger.

To ensure that there is minimal contribution from the slanted position of the finger, an initial contact area of 1×1 cm is established before sliding and recording friction measurements. As the PDMS finger is a soft object, the portion in contact with a surface flattens and the contact area remains largely unchanged during sliding. Any additional stick-slip after this alignment step is caused by contact aging at the interface, but the first trace we collect is always discarded to only consider stick-slip events caused by surface chemistry. We recognize that it is difficult to completely control the pressure distribution due to the planar interface, but this is also expected when humans freely explore a surface.

Comment 3, Part 4

In fact, if you look at the regime maps, there is very little space that has steady sliding. This does not represent well human exploration of surfaces. We do not tend to use a force and velocity that will cause extensive stick-slip (frequent regions of 100% stick-slip) and, in fact, the speeds used in the study are on the slow side, which also contributes to more stick-slip. At higher speeds and lower forces, all of the materials had steady sliding regions.

We are not aware of published studies that extensively show that humans avoid stickslip regimes. In fact, we are aware familiar with literature where stiction spike formation is suppressed – a recent paper by AliAbbasi, Basdogan et. al. investigates electroadhesion and friction with NaCl solution-infused interfaces, resulting in significantly steadier forces(17). We also directly showed evidence of instability formation that we observed during human exploration in Fig. 3B-C. These dynamic events are common, despite the lack of control of normal forces and sliding velocities. We also note that Reviewer 1, Comment 2, was suggesting that we further explore possible trends from parameterizing the stiction spike.

We note that many studies have often not gone at the velocities and masses required for stiction spikes – even though these masses and velocities would be routinely seen in free exploration – this is usually due to constraints of equipment(18). Sliding events during human free exploration of surfaces can exceed 100 mm/s for rapid touches. However, for the surfaces investigated here, we observe that large regions of stick-slip can emerge at velocities as low as 5 mm/s depending on the applied load. The incidence of steady sliding appears more dependent on the applied mass, with almost no steady sliding observed at or above 75 g. Indeed, the force categorization along our transition zones is the main point of the paper.

Comment 3, Part 5

Further, on these very smooth surfaces, the friction and stiction are more complex and cannot dismiss considerations such as finger material property change with sweat pore occlusion and sweat capillary forces. Also, the vertical motion of both the PDMS finger and the instructed human subjects is not the motion that humans typically use to discriminate between surfaces.

We did not describe the task sufficiently. Humans were only given the instruction to slide their finger along a single axis from top to bottom of a sample, not vertical as in azimuthal to gravity. We have updated our wording in the manuscript to reflect this.

Our changes to the manuscript (Page 4)

“Participants could touch for as long as they wanted, but were asked to only use their dominant index fingers along a single axis to better mimic the conditions for instability formation during mechanical testing with the mock finger.”

(Page 11)

“The participant was then asked to explore each sample simultaneously, and ran over each surface in strokes along a single axis until the participant could decide which of the two had “more friction”.”

Comment 3, Part 6

Finally, fingerprints may not affect the shape and size of the contact area, but they certainly do affect the dynamic response and detection of vibrations.

We are aware of the nuance. Our previous work on the role of fingerprints on friction experienced by a PDMS mock finger showed enhanced signals with the incorporation of ridges on the finger and used a rate-and-state model of a heterogenous, elastic body to find corresponding trends (though there is no existing model of friction that can accurately model experiments on mesoscale friction)(7). The key conclusion was that a flat finger still preserved key dynamic features, and the presence of stronger or more vibrations could result in more similar forces for different surfaces depending on the sliding conditions.

This is also in the context that we are seeking to provide a reasonable and experimentally accessible method to characterize surfaces, which will always be better as we get closer in replicating a true human finger. But our goal here was to replicate the finger sufficiently for use in human studies. We believe the more appropriate metric of success is if the mock finger is more successful than replacing traditional characterization experiments, like friction coefficient, roughness, surface energy, etc.

Comment 4

This all leads to the critical question, why are friction, normal force, and velocity not measured during the measured human exploration and in a systematic study using the real human finger? The authors posed an extremely interesting hypothesis that humans may alter their speed to feel the instability transition regions. This is something that could be measured with a real finger but is not likely to be correlated accurately enough to match regime boundaries with such a simplified artificial finger.

We are excited that our manuscript offers a tractable manner to test the hypothesis that tactile decision-making models use friction instabilities as evidence. However, we lay out the challenges and barriers, and how the scope of this paper will lead us in that direction. We also clarify that our goals are to provide a method to characterize samples to better design tactile interfaces in haptics or in psychophysical experiments and raise awareness that the common methods of sample characterization in touch by an average friction coefficient or roughness is fundamentally unsound.

In short, in our view, to further support our findings on instabilities would require answering:

(1) Which one, or combination of, of the multiple swipes that people make responsible for a tactile decision? (The need for a decision-making model)

(2) Establish what is, or may be, tactile evidence.

(3) Establish tactile decision-making models are similar or different than existing decision-making models.

(4) Test the hypothesis, in these models, that friction instabilities are evidence, and not some other unknown metric. This requires design samples that vary in the amount of evidence generated, but this evidence cannot be controlled directly. Rather, the samples indirectly vary evidence by how likely it is for a human to generate different types of friction instabilities during standard exploration.

(5) Design a task that does not require the use of subjective tactile descriptors, like “which one feels rougher”, which we see cause confusion in participants, which will likely require accounting for memory effects.

We elaborate these points below:

To successfully perform this experiment, we note that freely exploring humans make multiple strokes on a surface. Therefore, we would need to construct a decision-making model. It has not yet been demonstrated whether tactile decision making follows visual decision making, but perhaps to start, we can assume it does. Then, in the design of our decision-making paradigm, we immediately run into the problem: What is tactile evidence?

From Fig. 3C, we already can see that identifying evidence is challenging. Prior to this manuscript, people may have chosen the average force, or the highest force. Or we may choose the average friction force. Then, after deciding on the evidence, we need to find a method to manipulate the evidence, i.e., create samples or a machine that causes high friction, etc. We show that during the course of human touch, due to the dynamic nature of friction, the average can change a large amount and sample design becomes a central barrier to experiments. Others may suggest immobilizing the finger and applying a known force, but given how much friction changes with human exploration, there is no known method to make a machine recreate temporally and spatially varying friction forces during sliding onto a stationary finger. Finally, perhaps most importantly, in addition to mechanical challenges, a study by Liu, Colgate et al. showed that even if they recorded the friction (2D) of a finger exploring a surface and then replicated the same friction forces onto a finger, the participant could not determine which surface the replayed friction force was supposed to represent.1 This supports that the efference copy is important, that the forces in response to expected motion are important to determine friction. Finally, there is no known method to design instabilities a priori. They must be found through experiments. Especially since if we were to introduce, say a bump or a trough, then we bring in confounding variables to how participants tell surfaces apart.

Furthermore, even if we had some consistent method to create tactile “evidence”, the paradigm also deserves some consideration. In our experience, the 3-AFC task we perform is important because the vocabulary for touch has not been established. That is, in 3-AFC, by asking to determine which one sample is unlike the others, we do not have to ask the participant questions like “which one is rougher” or “which one has less friction”. In contrast, 2-AFC, which is better for decision-making models because it does not include memory, requires the asking of a perceptual question like: “which one is rougher?”. In our ongoing work, taking two silane coatings, we found that participants could easily identify which surface is unlike the others above chance in a 3-AFC, but participants, even within their own trials, could not consistently identify one silane as perceptually “rougher” by 2-AFC. To us, this calls into question the validity of tactile descriptors, but is beyond the scope of this manuscript.

This is not our only goal, but in the context of human exploration, in this manuscript here, we believed it was important to identify a mechanical parameter that was consistent with how humans explore surfaces, but was also a parameter that could characterize to some consistent property of a surface – irrespective of whether a human was touching it. We thought that designing human decision-making models and paradigms around the friction coefficient would not be successful.

Given the scope of these challenges, we do not think it would be possible to establish these conceptual sequences in a single manuscript.

Reviewer 2 (Public review):

Summary:

In this paper, the authors want to test the hypothesis that frictional instabilities rather than friction are the main drivers for discriminating flat surfaces of different sub-nanometric roughness profiles.

They first produced flat surfaces with 6 different coatings giving them unique and various properties in terms of roughness (picometer scale), contact angles (from hydrophilic to hydrophobic), friction coefficient (as measured against a mock finger), and Hurst exponent.

Then, they used those surfaces in two different experiments. In the first experiment, they used a mock finger (PDMS of 100kPA molded into a fingertip shape) and slid it over the surfaces at different normal forces and speeds. They categorized the sliding behavior as steady sliding, sticking spikes, and slow frictional waves by visual inspection, and show that the surfaces have different behaviors depending on normal force and speed. In a second experiment, participants (10) were asked to discriminate pairs of those surfaces. It is found that each of those pairs could be reliably discriminated by most participants.

Finally, the participant's discrimination performance is correlated with differences in the physical attributes observed against the mock finger. The authors found a positive correlation between participants' performances and differences in the count of steady sliding against the mock finger and a negative correlation between participants' reaction time and differences in the count of stiction spikes against the mock finger. They interpret those correlations as evidence that participants use those differences to discriminate the surfaces.

Strengths:

The created surfaces are very interesting as they are flat at the nanometer scale, yet have different physical attributes and can be reliably discriminated.”

We thank Reviewer 2 for their notes on our manuscript. The responses below address the reviewer’s comments and recommendations for revised work.

Weaknesses:

Comment 1

In my opinion, the data presented in the paper do not support the conclusions. The conclusions are based on a correlation between results obtained on the mock finger and results obtained with human participants but there is no evidence that the human participants' fingertips will behave similarly to the mock finger during the experiment. Figure 3 gives a hint that the 3 sliding behaviors can be observed in a real finger, but does not prove that the human finger will behave as the mock finger, i.e., there is no evidence that the phase maps in Figure 1C are similar for human fingers and across different people that can have very different stiffness and moisture levels.

The mechanical characterization conducted with the mock finger seeks to extract significant features of friction traces of a set of surfaces to use as predictors of tactile discriminability. The goal is to find a consistent method to characterize surfaces for use in tactile experiments that can be replicated by others and used prior to any human experiments. However, in the overall response and in a response to a similar comment by Reviewer 1, we also explain why we believe experiments on humans to establish this fact is not yet reasonable.

Comment 2

I believe that the authors collected the contact forces during the psychophysics experiments, so this shortcoming could be solved if the authors use the actual data, and show that the participant responses can be better predicted by the occurrence of frictional instabilities than by the usual metrics on a trial by trial basis, or at least on a subject by subject basis. I.e. Poor performers should show fewer signs of differences in the sliding behaviors than good performers.

To fully implement this, a decision-making model is necessary because, as a counter example, a participant could have generated 10 swipes of SFW and 1 swipe of a Sp, but the Sp may have been the most important event for making a tactile decision. This type of scenario is not compatible with the analysis suggested — and similar counterpoints can be made for other types of seemingly straightforward analysis.

While we are interested and actively working on this, the study here is critical to establish types of evidence for a future decision-making model. We know humans change their friction constantly during real exploration, so it is unclear which of these constantly changing values we should input into the decision making model, and the future challenges we anticipate are explained in Comment 1.

Comment 3

The sample size (10) is very small.

We recognize that, with all factors being equal, this sample size is on the smaller end. However, we emphasize the degree of control of samples is far above typical, with minimal variations in sample properties such as surface roughness, and every sample for every trial was pristine. Furthermore, the sample preparation (> 300 individual wafers were used) and cost became a factor. Although not typically appropriate, and thus not included in the manuscript, a post-hoc power analysis for our 100 trials of our pair that was closest to chance, P4, (53%, closest to chance at 33%) showed a power of 98.2%, suggesting that the study was appropriately powered.

Reviewer 2 (Recommendations for the authors):

Comment 1

Differences in SS and Sp (Table 2) are NOT physical or mechanical differences but are obtained by counting differences in the number of occurrences of each sliding behavior. It is rather a weird choice.

We disagree that differences in SS and Sp are not physical or mechanical, as these are well-established phenomena in the soft matter and tribology literature(19-21). These are known as “mechanical instabilities” and generated due to the effects of two physical phenomena: the elasticity of the finger (which is constant in our mechanical testing) and the friction forces present (which change per sample type). The motivation behind using these different shapes is that the instabilities, in some conditions, can be invariant to external factors like velocity. This would be quite advantageous for human exploration because, unlike friction coefficient, which changes with nearly any factor, including velocity and mass, the instabilities being invariant to velocity would mean that we are accurately characterizing a unique identifier of the surface even though velocity may be variable.

This “weird choice” is the central innovation of this paper. This choice was necessary because we demonstrated that the common usage of friction coefficient is fundamentally flawed: we see that friction coefficient suggests that surface which are more different would feel more similar – indeed the most distinctive surfaces would be two surfaces that are identical, which is clearly spurious. One potential explanation for why we were able to see this is effect is because our surfaces have similar (< 0.6 nm variability) roughness, removing potential confounding factors, and this type of low roughness control has not been used in tactile studies to the best of our knowledge.

Comment 2

Figures 2B-C: why are the x-data different than Table 2?

The x-data in Fig. 2B-C are the absolute differences in the number of occurrences measured for a given instability type or material property out of 144 pulls. Modeling the human participant results in our GLMMs required the independent variables to be in this form rather than percentages. We initially chose to list percent differences in Table 2 to highlight the ranges of differences instead of an absolute value, but have added both for clarity.

Our changes to the manuscript (Page 7)

“To determine if humans can detect these three different instabilities, we selected six pairs of surfaces to create a broad range of potential instabilities present across all three types. These are summarized in Table 2, where the first column for each instability is the difference in occurrence of that instability formed between each pair, and the second is the percent difference.”

Comment 3

"We constructed a set of coated surfaces with physical differences which were imperceptible by touch but created different types of instabilities based on how quickly a finger is slid and how hard a human finger is pressed during sliding." Yet, in your experiment, participants could discriminate them, so this is incoherent.

To clarify the point, macroscopic objects can differ in physical shape and in chemical composition. What we meant was that the physical differences, i.e., roughness, were below a limit (Skedung et al.) that participants, without a coating, would not be able to tell these apart(22). Therefore, the reason people could tell our surfaces apart was due to the chemical composition of the surface, and not any differences in roughness or physical effects like film stiffness (due to the molecular-scale thinness of the surface coatings, they are mechanically negligible). However, we concede that at the molecular scale, the traditional macroscopic distinction between physical and chemical is blurred.

We have made minor revisions to the wording in the abstract. We clarify that the surface coatings had physical differences in roughness that were smaller than 0.6 nm, which based purely on roughness, would not be expected to be distinguishable to participants. Therefore, the reason participants can tell these surfaces apart is due to differences in friction generated by chemical composition, and we were able to minimize contributions from physical differences in the sample our study.

Our changes to the manuscript (Page 1, Abstract)

“We constructed a set of coated surfaces with minimal physical differences that by themselves, are not perceptible to people, but instead, due to modification in surface chemistry, the surfaces created different types of instabilities based on how quickly a finger is slid and how hard a human finger is pressed during sliding.”

Reviewer 3 (Public review):

Strengths:  

The paper describes a new perspective on friction perception, with the hypothesis that humans are sensitive to the instabilities of the surface rather than the coefficient of friction. The paper is very well written and with a comprehensive literature survey.

One of the central tools used by the author to characterize the frictional behavior is the frictional instabilities maps. With these maps, it becomes clear that two different surfaces can have both similar and different behavior depending on the normal force and the speed of exploration. It puts forward that friction is a complicated phenomenon, especially for soft materials.

The psychophysics study is centered around an odd-one-out protocol, which has the advantage of avoiding any external reference to what would mean friction or texture for example. The comparisons are made only based on the texture being similar or not.

The results show a significant relationship between the distance between frictional maps and the success rate in discriminating two kinds of surface.”

We thank Reviewer 3 for their notes and interesting discussion points on our manuscript. Below, we address the reviewer’s feedback and comments on related works.

Weaknesses:

Comment 1

The main weakness of the paper comes from the fact that the frictional maps and the extensive psychophysics study are not made at the same time, nor with the same finger. The frictional maps are produced with an artificial finger made out of PDMS which is a poor substitute for the complex tribological properties of skin.

A similar comment was made by Reviewers 1 and 2 and parts are replicated below. We are not claiming that our PDMS fingers are superior to real fingers, but rather, we cannot establish standards in the field by using real human fingers that vary between subjects and researchers. We believe the mock finger we designed is a reasonable mimic of the human finger by matching surface energy, heterogeneous mechanical structure, and the ability to test multiple physiologically relevant pressures and sliding velocities.

We achieve a heterogeneous mechanical structure with the 3 primary components of stiffness of a human finger. The effective modulus of ~100 kPa, from soft tissue,8,9 is obtained with a 30:1 ratio of PDMS to crosslinker. The PDMS also surrounds a rigid, acrylic bone comparable to the distal phalanx, which provides an additional layer of higher modulus.10 Additionally, the 8-hour UV-Ozone treatment decreases the viscoelastic tack of the pristine PDMS by glassifying, or further crosslinking the surface of the finger,11 therefore imparting greater stiffness at the surface similar to the contributions of the stratum corneum, along with a similar surface energy.12 The finger is used at least a day after UV-Ozone treatment is completed in order for the surface to return to moderate hydrophilicity, similar to the outermost layer of human skin.16 We also discuss the shape of the contact formed. To ensure that there is minimal contribution from the slanted position of the finger, an initial contact area of 1×1 cm is established before sliding and recording friction measurements. As the PDMS finger is a soft object, the portion in contact with a surface flattens and the contact area remains largely unchanged during sliding. We recognize that it is difficult to completely control the pressure distribution due to the planar interface, but this variation is also expected when humans freely explore a surface. Finally, we consider flat vs. fingerprinted fingers. Our previous work on the role of fingerprints on friction experienced by a PDMS mock finger showed enhanced signals with the incorporation of ridges on the finger and used a rate-andstate model of a heterogenous, elastic body to find corresponding trends.7 The key conclusion was that a flat finger still preserved key dynamic features, and the presence of stronger or more vibrations could result in more similar forces for different surfaces depending on the sliding conditions. We note that we have subsequently used the controlled mechanical data collected with this flat mock finger in correlations with human psychophysics in previous work, where findings from our mechanical experiments were predictive of human performance.3–6 Ultimately, we see from our prior work and here that, despite the drawbacks of our mock finger, it outperforms other standard characterization technique in providing information about the mesoscale that correlates to tactile perception. We have added these details to the manuscript.

We also note that an intermediate option, replicating real fingers, even in a mold, may also inadvertently limit trends from characterization to a specific finger. One of the main – and severe – limitations of using a human finger is that all fingers are different, meaning any study focusing on a particular user may not apply to others or be recreated easily by other researchers. We cannot set a standard for replication around a real human finger as that participant may no longer be available, or willing to travel the world as a “standard”. Furthermore, the method in which a single person changes their pressures and velocities as they touch a surface is highly variable. We also note that in the Summary Response, we noted that a study by Colgate et al. (IEEE ToH 2024) demonstrated that efference copies may be important, and thus constraining a human finger and replaying the forces recorded during free exploration will not lead to the participant identifying a surface with any consistency. Thus, it is important to allow humans to freely explore surfaces, but creates nearly limitless variability in friction forces.

This is also against the backdrop that we are seeking to provide a method to characterize surfaces, which will be aided as we get closer in replicate a true human finger. Indeed, the more features we replicate, the more successful the mechanical data will be in correlating to tactile distinguishability. But reasonably, our success would be in replacing traditional characterization experiments, not in recreating the forces of an arbitrary human finger.

Our changes to the manuscript Added (Page 2-3)

“Mock finger as a characterization tool

In this work, we use a mechanical setup with a PDMS mock finger to derive tactile predictors from controlled friction traces alternative to average friction coefficients. While there is a tradeoff in selecting a synthetic finger over a more accurate, real human finger in modeling touch, our aim to design a method of mesoscale surface characterization for more successful studies on tactile perception cannot be fulfilled using one human participant as a standard. We believe that with sufficient replication of surface and bulk properties as well as contact geometry, and controlled friction measurements collected at loading conditions observed during a tactile discrimination task, we can isolate unique frictional features of a set of surfaces that do not arise from human-to-human variability.

The major component of a human finger, by volume, is soft tissue (~56%)(22), resulting in an effective modulus close to 100 kPa(23,24). In order to achieve this same softness, we crosslink PDMS in a 1×1×5 cm mold at a 30:1 elastomer:crosslinker ratio. However, two more features impart increased stiffness in a human finger. Most of this added rigidity is derived from the bone at the fingertip, the distal phalanx(23-25), which we mimic with an acrylic bone within our PDMS network. The stratum corneum, the stiffer, glassier outer layer of skin(26), is replicated with the surface of the mock finger glassified, or further crosslinked, after 8 hours of UV-Ozone treatment(27). This treatment also modifies the surface properties of the native PDMS to align with those of a human finger more closely. It minimizes the viscoelastic tack at the surface, resulting in a comparable non-sticky surface. At least one day after treatment, the finger surface returns to moderate hydrophilicity (~60º), as is typically observed for a real finger(28).

The initial contact area formed before a friction trace is collected is a rectangle of 1×1 cm. While this shape is not entirely representative of a human finger with curves and ridges, human fingers flatten out enough to reduce the effects of curvature with even very light pressures(28-30). This implies that regardless of finger pressure, the contact area is largely load-independent, which is more accurately replicated with a rectangular mock finger. It is still a challenge to control pressure distribution with this planar interface, but non-uniform pressures are also expected during human exploration.

Lastly, we consider fingerprints vs. flat fingers. A key finding of our previous work is that while fingerprints enhanced frictional dynamics at certain conditions, key features were still maintained with a flat finger(7). Furthermore, for some loading conditions, the more amplified signals could also result in more similar friction traces for different surfaces. We have continued to use flat fingers in our mechanical experiments, and have observed good agreement between these friction traces and human experiments(7,8,21,31).”

(Page 3-4, Materials and Methods)

“Mock Finger Preparation

Friction forces across all six surfaces were measured using a custom apparatus with a polydimethylsiloxane (PDMS, Dow Sylgard 184) mock finger that mimics a human finger’s

mechanical properties and contact mechanics while exploring a surface relatively closely(7,8). PDMS and crosslinker were combined in a 30:1 ratio to achieve a stiffness of 100 kPa comparable to a real finger, then degassed in a vacuum desiccator for 30 minutes. We are aware that the manufacturer recommended crosslinking ratio for Sylgard 184 is 10:1 due to potential uncrosslinked liquid residues(32), but further crosslinking concentrated at the surface prevents this. The prepared PDMS was then poured into a 1×1×5 cm mold also containing an acrylic 3D-printed “bone” to attach applied masses on top of the “fingertip” area contacting a surface during friction testing. After crosslinking in the mold at 60ºC for 1 hour, the finger was treated with UV-Ozone for 8 hours out of the mold to minimize viscoelastic tack.  

Mechanical Testing

A custom device using our PDMS mock finger was used to collect macroscopic friction force traces replicating human exploration(7,8). After placing a sample surface on a stage, the finger was lowered at a slight angle such that an initial 1×1 cm rectangle of “fingertip” contact area could be established. We considered a broad range of applied masses (M \= 0, 25, 75, and 100 g) added onto the deadweight of the finger (6 g) observed during a tactile discrimination task. The other side of the sensor was connected to a motorized stage (V-508 PIMag Precision Linear Stage, Physikinstrumente) to control both displacement (4 mm across all conditions) and sliding velocity (v \= 5, 10, 25, and 45 mm s^-1). Forces were measured at all 16 combinations of mass and velocity via a 250 g Futek force sensor (k \= 13.9 kN m^-1) threaded to the bone, and recorded at an average sampling rate of 550 Hz with a Keithley 7510 DMM digitized multimeter. Force traces were collected in sets of 4 slides, discarding the first due to contact aging. Because some mass-velocity combinations were near the boundaries of instability phase transitions, not all force traces at these given conditions exhibited similar profiles. Thus, three sets were collected on fresh spots for each condition to observe enough occurrences of multiple instabilities, at a total of nine traces per combination for each surface.”

Added References (Page 13)

M. Murai, H.-K. Lau, B. P. Pereira and R. W. H. Pho, J. Hand Surg., 1997, 22, 935–941.

A. Abdouni, M. Djaghloul, C. Thieulin, R. Vargiolu, C. Pailler-Mattei and H. Zahouani, R. Soc. Open Sci., DOI:10.1098/rsos.170321.

P.-H. Cornuault, L. Carpentier, M.-A. Bueno, J.-M. Cote and G. Monteil, J. R. Soc. Interface, DOI:10.1098/rsif.2015.0495.

K. Qian, K. Traylor, S. W. Lee, B. Ellis, J. Weiss and D. Kamper, J. Biomech., 2014, 47, 3094– 3099.

Y. Yuan and R. Verma, Colloids Surf. B Biointerfaces, 2006, 48, 6–12.

Y.-J. Fu, H. Qui, K.-S. Liao, S. J. Lue, C.-C. Hu, K.-R. Lee and J.-Y. Lai, Langmuir, 2010, 26, 4392–4399.

Comment 2

The evidence would have been much stronger if the measurement of the interaction was done during the psychophysical experiment. In addition, because of the protocol, the correlation is based on aggregates rather than on individual interactions.

Our Response: We agree that this would have helped further establish our argument, but in the overall statement and in other reviewer responses, we describe the significant challenges to establishing this.

To fully implement this, a decision-making model is necessary because, as a counter example, a participant could have generated 10 swipes of SFW and 1 swipe of a Sp, but the Sp may have been the most important event for making a tactile decision. We also clarify that our goals are to provide a method to characterize samples to better design tactile interfaces in haptics or in psychophysical experiments.

In short, in our view, to develop a decision-making model, the challenges are as follows:

(1) Which one, or combination of, of the multiple swipes that people make responsible for a tactile decision?

(2) Establish what is, or may be, tactile evidence.

(3) Establish tactile decision-making models are similar or different than existing decision-making models.

(4) Test the hypothesis, in these models, that friction instabilities are evidence, and not some other unknown metric.

(5) Design a task that does not require the use of subjective tactile descriptors, like “which one feels rougher”, which we see cause confusion in participants, which will likely require accounting for memory effects.

(6) Design samples that vary in the amount of evidence generated, but this evidence cannot be controlled directly. Rather, the samples indirectly vary evidence by how likely it is for a human to generate different types of friction instabilities during standard exploration.

We elaborate these points below:

To successfully perform this experiment, we note that freely exploring humans make multiple strokes on a surface. Therefore, we would need to construct a decision-making model. It has not yet been demonstrated whether tactile decision making follows visual decision making, but perhaps to start, we can assume it does. Then, in the design of our decision-making paradigm, we immediately run into the problem: What is tactile evidence?

From Fig. 3C, we already can see that identifying evidence is challenging. Prior to this manuscript, people may have chosen the average force, or the highest force. Or we may choose the average friction force. Then, after deciding on the evidence, we need to find a method to manipulate the evidence, i.e., create samples or a machine that causes high friction, etc. We show that during the course of human touch, due to the dynamic nature of friction, the average can change a large amount and sample design becomes a central barrier to experiments. Others may suggest to immobilize the finger and applying a known force, but given how much friction changes with human exploration, there is no known method to make a machine recreate temporally and spatially varying friction forces during sliding onto a stationary finger. Finally, perhaps most importantly, in addition to mechanical challenges, a study by Liu, Colgate et al. showed that even if they recorded the friction (2D) of a finger exploring a surface and then replicated the same friction forces onto a finger, the participant could not determine which surface the replayed friction force was supposed to represent.1 This supports that the efference copy is important, that the forces in response to expected motion are important to determine friction. Finally, there is no known method to design instabilities a priori. They must be found through experiments, especially since if we were to introduce, say a bump or a trough, then we bring in confounding variables to how participants tell surfaces apart.

Furthermore, even if we had some consistent method to create tactile “evidence”, the paradigm also deserves some consideration. In our experience, the 3-AFC task we perform is important because the vocabulary for touch has not been established. That is, in 3-AFC, by asking to determine which one sample is unlike the others, we do not have to ask the participant questions like “which one is rougher” or “which one has less friction”. In contrast, 2-AFC, which is better for decision-making models because it does not include memory, requires the asking of a perceptual question like: “which one is rougher?”. In our ongoing work, taking two silane coatings, we found that participants could easily identify which surface is unlike the others above chance in a 3-AFC, but participants, even within their own trials, could not consistently identify one silane as perceptually “rougher” by 2-AFC. To us, this calls into question the validity of tactile descriptors, but is beyond the scope of the current manuscript.

This is not our only goal, but in the context of human exploration, in this manuscript here, we believed it was important to identify a mechanical parameter that was consistent with how humans explore surfaces, but was also a parameter that could characterize to some consistent property of a surface – irrespective of whether a human was touching it. We thought that designing human decision-making models and paradigms around the friction coefficient would not be successful.

Given the scope of these challenges, we do not think it would be possible to establish this conceptual sequence in a single manuscript.

Comment 3

The authors compensate with a third experiment where they used a 2AFC protocol and an online force measurement. But the results of this third study, fail to convince the relation.

With this experiment, our central goal was to demonstrate that the instabilities we have identified with the PDMS finger also occur with a human finger. Several instances of SS, Sp, and SFW were recorded with this setup as a participant touched surfaces in real time.

Comment 4

No map of the real finger interaction is shown, bringing doubt to the validity of the frictional map for something as variable as human fingers.

Real fingers change constantly during exploration, and friction is state-dependent, meaning that the friction will depend on how the person was moving the moment prior. Therefore, a map is only valid for a single human movement – even if participants all were instructed to take a single swipe and start from zero motion, humans are unable to maintain constant velocities and pressures. Clearly, this is not sustainable for any analysis, and these drawbacks apply to any measured parameter, whether instabilities suggested here, or friction coefficients used throughout. We believe the difficulty of this approach emphasizes why a standard map of characterization of a surface by a mock finger, even with its drawbacks, is a viable path forward.

Reviewer 3 (Recommendations for the authors):

Comment 1

It would be interesting to comment on a potential connection between the frictional instability maps and Schalamack waves

Schallamach waves are a subset of slow frictional waves (SFW). Schallmach waves are very specifically defined. They are a are pockets of air that form between a soft sliding object and rigid surface, and propagate rear-to-front (retrograde waves) as a soft object is slid and buckles due to adhesive pinning. Wrinkles form at the detached portion of the soft material, until the interface reattaches and the process repeats.23 There is typically a high burden of proof to establish a Schallamach wave over a more general slow frictional wave. We note that it would be exceeding difficult to design samples that can reliably create subsets of SFW, but we are aware that this may be an interesting question at a future point in our work.

Comment 2

The force sensors look very compliant, and given the dynamic nature of the signal, it is important to characterize the frequency response of the system to make sure that the fluctuations are not amplified.

Our Response: Thank you for noticing. We mistyped the sensor spring constant as 13.9 N m^-1 instead of kN m^-1. However, below we show how the instabilities are derived from the mechanics at the interface due to the compliance of the finger. The “springs” of the force sensor and PDMS finger are connected in parallel. Since k_sensor = 13.9 kN m^-1, the spring constant of the system overall reflects the compliance of the finger, and highlights the oscillations arising solely from stick-slip. A sample calculation is shown below.

Author response image 1.

Fitting a line to the initial slope of the force trace for C6 gives the equation y = 25.679_x_ – 0.2149. The slope here represents force data over time data, and is divided by the velocity (25 mm/s) to determine 𝐹𝐹 the spring constant of the system . This value is lower than ksensor = 13.9 kN/m, indicating that the “springs” representing the force sensor and PDMS finger are connected in parallel: . The finger is the compliant component of the system, with k_finger = 0.902 N/m, and of course, real human fingers are also compliant so this matches our goals with the design of the mock finger.

Our changes to the manuscript (Page 4)

(k \= 13.9 kN m^-1)

Comment 3

The authors should discuss about the stochastic nature of friction:

Wiertlewski, Hudin, Hayward, IEEE WHC 2011

Greenspon, McLellan, Lieber, Bensmaia, JRSI 2020”

We believe that, given the references, this comment on “stochastic” refers to the macroscopically-observable fluctuations (i.e., the mechanical “noise” which is not due to instrument noise) in friction arising from the discordant network of stick-slip phenomena occurring throughout the contact zone, and not the stochastic nature of nanoscale friction that occurs thermal fluctuations nor due to statistical distributions in bond breaking associated with soft contact.

We first note that our small-scale fluctuations do not arise from a periodic surface texture that dominates in the frequency regime. However, even on our comparatively smooth surfaces, we do expect fluctuations due to nanoscale variation in contact, generation of stick-slip across at microscale length scales that occur either concurrently or discordantly across the contact zone, and the nonlinear dependence of friction to nearly any variation in state and composition(7).

Perhaps the most relevant to the manuscript is that a major advantage of analysis by friction is that it sidesteps these ever-present microscale fluctuations, leading to more clearly defined classifiers or categories during analysis. Wiertlewski et. al. showed repeated measurements in their systems ultimately gave rise to consistent frequencies(24) (we think their system was in a steady sliding regime and the patterning gave rise to underlying macroscopic waves). These consistent frequencies, at least in soft systems and absent obvious macroscopic patterned features, would be expected to arise from the instability categories and we see them throughout.

Comment 4

It is stated that "we observed a spurious, negative correlation between friction coefficient and accuracy”.

What makes you qualify that correlation as spurious?

We mean this as in the statistical definition of “spurious”.

This correlation would indicate that by the metric of friction coefficient, more different surfaces are perceived more similarly. Thus, two very different surfaces, like Teflon and sandpaper, by friction coefficient would be expected to feel very similar. Two nearly identical surfaces would be expected to feel very different – but of course, humans cannot consistently distinguish two identical surfaces. This finding is counterintuitive and refutes that friction coefficient is a reliable classifier of surfaces by touch. We do not think it is productive to determine a mechanism for a spurious correlation, but perhaps one reason we were able to observe this is because our study, to the best of our knowledge, is unique for having samples that are controlled in their physical differences in roughness and surface features.

Our changes to the manuscript (Page 10)

“To compare the value of looking at frictional instabilities, we also performed GLMM fits on common approaches in the field, like a friction coefficient or material property typically used in tactile discrimination, shown in Fig. 2D-E. Interestingly, in Fig. 2D, we observed a spurious, negative correlation between friction coefficient (typically and often problematically simplified as across all tested conditions) and accuracy (r = -0.64, p < 0.01); that is, the more different the surfaces are by friction coefficient, the less people can tell them apart. This spurious correlation would be the opposite of intuition, and further calls into question the common practice of using friction coefficients in touch-related studies. The alternative, two-term model which includes adhesive contact area for friction coefficient(29) was even less predictive (see Fig. S6A of SI). We believe such a correlation could not have been uncovered previously as our samples are minimal in their physical variations. Yet, the dynamic changes in force even within a single sample are not considered, despite being a key feature of mesoscale friction during human touch.

We investigate different material properties in Fig. 2E. Differences in average roughness R_a (or other parameters, like root mean square roughness R_rms (Fig. S6A of SI) did not show a statistically significant correlation to accuracy. Though roughness is a popular parameter, correlating any roughness parameter to human performance here could be moot: the limit of detecting roughness differences has previously been defined as 13 nm on structured surfaces(33) and much higher for randomly rough surfaces(46), all of which are magnitudes larger than the roughness differences between our surfaces. The differences in contact angle hysteresis – as an approximation of the adhesion contributions(47) – do not present any statistically significant effects on performance.”

Comment 5

The authors should comment on the influence of friction on perceptual invariance. Despite inducing radially different frictional behavior for various conditions, these surfaces are stably perceived. Maybe this is a sign that humans extract a different metric?

We agree – we are excited that frictional instabilities may offer a more stable perceptual cue because they are not prone to fluctuations (Recommendations for the authors, Comment 3) and instability formation, in many conditions, is invariant to applied pressures and velocities – thus forming large zones where a human may reasonable encounter a given instability.

Raw friction is highly prone to variation during human exploration (in alignment with Recommendations for the authors, Comment 3), but ongoing work seeks to explain tactile constancy, or the ability to identify objects despite these large changes in force. Very recently published work by Fehlberg et. al. identified the role of modulating finger speed and normal force in amplifying the differences in friction coefficient between materials in order to identify them(25), and we postulate that their work may be streamlined and consistent with the idea of friction instabilities, though we have not had a chance to discuss this in-depth with the authors yet.

We think that the instability maps show a viable path forward to how surfaces are stably perceived, and instabilities themselves show a potential mechanism: mathematically, instabilities for given conditions can be invariant to velocity or mass, creating zones where a certain instability is encountered. This reduces the immense variability of friction to a smaller, more stable classification of surfaces (e.g., a 30% SS surface or a 60% SS surface). A given surface will typically produce the same instability at a specific condition (we found some boundaries are extremely condition sensitive, but many conditions are not), whereas a single friction trace which is highly prone to variation is not a stable metric.

Added References (Page 14)

53 M. Fehlberg, E. Monfort, S. Saikumar, K. Drewing and R. Bennewitz, IEEE Trans. Haptics, 2024, 17, 957–963.

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Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper is an elegant, mostly observational work, detailing observations that polysome accumulation appears to drive nucleoid splitting and segregation. Overall I think this is an insightful work with solid observations.

Thank you for your appreciation and positive comments. In our view, an appealing aspect of this proposed biophysical mechanism for nucleoid segregation is its self-organizing nature and its ability to intrinsically couple nucleoid segregation to biomass growth, regardless of nutrient conditions.

Strengths:

The strengths of this paper are the careful and rigorous observational work that leads to their hypothesis. They find the accumulation of polysomes correlates with nucleoid splitting, and that the nucleoid segregation occurring right after splitting correlates with polysome segregation. These correlations are also backed up by other observations:

(1) Faster polysome accumulation and DNA segregation at faster growth rates.

(2) Polysome distribution negatively correlating with DNA positioning near asymmetric nucleoids.

(3) Polysomes form in regions inaccessible to similarly sized particles.

These above points are observational, I have no comments on these observations leading to their hypothesis.

Thank you!

Weaknesses:

It is hard to state weaknesses in any of the observational findings, and furthermore, their two tests of causality, while not being completely definitive, are likely the best one could do to examine this interesting phenomenon.

It is indeed difficult to prove causality in a definitive manner when the proposed coupling mechanism between nucleoid segregation and gene expression is self-organizing, i.e., does not involve a dedicated regulatory molecule (e.g., a protein, RNA, metabolite) that we could have depleted through genetic engineering to establish causality. We are grateful to the reviewer for recognizing that our two causality tests are the best that can be done in this context.

Points to consider / address:

Notably, demonstrating causality here is very difficult (given the coupling between transcription, growth, and many other processes) but an important part of the paper. They do two experiments toward demonstrating causality that help bolster - but not prove - their hypothesis. These experiments have minor caveats, my first two points.

(1) First, "Blocking transcription (with rifampicin) should instantly reduce the rate of polysome production to zero, causing an immediate arrest of nucleoid segregation". Here they show that adding rifampicin does indeed lead to polysome loss and an immediate halting of segregation - data that does fit their model. This is not definitive proof of causation, as rifampicin also (a) stops cell growth, and (b) stops the translation of secreted proteins. Neither of these two possibilities is ruled out fully.

That’s correct; cell growth also stops when gene expression is inhibited, which is consistent with our model in which gene expression within the nucleoid promotes nucleoid segregation and biomass growth (i.e., cell growth), inherently coupling these two processes. This said, we understand the reviewer’s point: the rifampicin experiment doesn’t exclude the possibility that protein secretion and cell growth drive nucleoid segregation. We are assuming that the reviewer is envisioning an alternative model in which sister nucleoids would move apart because they would be attached to the membrane through coupled transcription-translation-protein secretion (transertion) and the membrane would expand between the separating nucleoids, similar to the model proposed by Jacob et al in 1963 (doi:10.1101/SQB.1963.028.01.048). There are several observations arguing against this cell elongation/transertion model.

(1) For this alternative mechanism to work, membrane growth must be localized at the middle of the splitting nucleoids (i.e., midcell position for slow growth and ¼ and ¾ cell positions for fast growth) to create a directional motion. To our knowledge, there is no evidence of such localized membrane incorporation. Furthermore, even if membrane growth was localized at the right places, the fluidity of the cytoplasmic membrane (PMID: 6996724, 20159151, 24735432, 27705775) would be problematic. To circumvent the membrane fluidity issue, one could potentially evoke an additional connection to the rigid peptidoglycan, but then again, peptidoglycan growth would have to be localized at the middle of the splitting nucleoid. However, peptidoglycan growth is dispersed early in the cell division cycle when the nucleoid splitting happens in fast growing cells and only appears to be zonal after the onset of cell constriction (PMID: 35705811, 36097171, 2656655).

(2) Even if we ignore the aforementioned caveats, Paul Wiggins’s group ruled out the cell elongation/transertion model by showing that the rate of cell elongation is slower than the rate of chromosome segregation (PMID: 23775792). In the revised manuscript, we wil clarify this point and provide confirmatory data showing that the cell elongation rate is indeed slower than the nucleoid segregation rate, indicating that it cannot be the main driver.

(3) Furthermore, our correlation analysis comparing the rate of nucleoid segregation to the rate of either cell elongation or polysome accumulation argues that polysome accumulation plays a larger role than cell elongation in nucleoid segregation. These data were already shown in Figure 1H and Figure 1 – figure supplement 3 of the original manuscript but were not highlighted in this context. We will revise the text to clarify this point.

(4) The asymmetries in nucleoid compaction that we described in our paper are predicted by our model. We do not see how they could be explained by cell growth or protein secretion.

(5) We also show that polysome accumulation at ectopic sites (outside the nucleoid) results in correlated nucleoid dynamics, consistent with our proposed mechanism. These nucleoid dynamics cannot be explained by cell growth or protein secretion (transertion).

(1a) As rifampicin also stops all translation, it also stops translational insertion of membrane proteins, which in many old models has been put forward as a possible driver of nucleoid segregation, and perhaps independent of growth. This should at last be mentioned in the discussion, or if there are past experiments that rule this out it would be great to note them.

It is not clear to us how the attachment of the DNA to the cytoplasmic membrane could alone create a directional force to move the sister nucleoids. We agree that old models have proposed a role for cell elongation (providing the force) and transertion (providing the membrane tether).  Please see our response above for the evidence (from the literature and our work) against it. This was mentioned in the introduction and Results section, but we agree that this was not well explained. We will add experimental data and revise the text to clarify these points.

(1b) They address at great length in the discussion the possibility that growth may play a role in nucleoid segregation. However, this is testable - by stopping surface growth with antibiotics. Cells should still accumulate polysomes for some time, it would be easy to see if nucleoids are still segregated, and to what extent, thereby possibly decoupling growth and polysome production. If successful, this or similar experiments would further validate their model.

We reviewed the literature and could not find a drug that stops cell growth without stopping gene expression. Any drug that affects the membrane integrity or potential stops gene expression, which requires ATP.  However, our experiment in which we drive polysome accumulation at ectopic sites decouples polysome accumulation from cell growth. In this experiment, by redirecting most of chromosome gene expression to a single plasmid-encoded gene, we reduce the rate of cell growth but still create a large accumulation of polysomes at an ectopic location. This ectopic polysome accumulation is sufficient to affect nucleoid dynamics in a correlated fashion. In the revised manuscript, we will clarify this point and add model simulations to show that our experimental observations are predicted by our model.

(2) In the second experiment, they express excess TagBFP2 to delocalize polysomes from midcell. Here they again see the anticorrelation of the nucleoid and the polysomes, and in some cells, it appears similar to normal (polysomes separating the nucleoid) whereas in others the nucleoid has not separated. The one concern about this data - and the differences between the "separated" and "non-separated" nuclei - is that the over-expression of TagBFP2 has a huge impact on growth, which may also have an indirect effect on DNA replication and termination in some of these cells. Could the authors demonstrate these cells contain 2 fully replicated DNA molecules that are able to segregate?

We will perform the requested experiment.

(3) What is not clearly stated and is needed in this paper is to explain how polysomes do (or could) "exert force" in this system to segregate the nucleoid: what a "compaction force" is by definition, and what mechanisms causes this to arise (what causes the "force") as the "compaction force" arises from new polysomes being added into the gaps between them caused by thermal motions.

They state, "polysomes exert an effective force", and they note their model requires "steric effects (repulsion) between DNA and polysomes" for the polysomes to segregate, which makes sense. But this makes it unclear to the reader what is giving the force. As written, it is unclear if (a) these repulsions alone are making the force, or (b) is it the accumulation of new polysomes in the center by adding more "repulsive" material, the force causes the nucleoids to move. If polysomes are concentrated more between nucleoids, and the polysome concentration does not increase, the DNA will not be driven apart (as in the first case) However, in the second case (which seems to be their model), the addition of new material (new polysomes) into a sterically crowded space is not exerting force - it is filling in the gaps between the molecules in that region, space that needs to arise somehow (like via Brownian motion). In other words, if the polysome region is crowded with polysomes, space must be made between these polysomes for new polysomes to be inserted, and this space must be made by thermal (or ATP-driven) fluctuations of the molecules. Thus, if polysome accumulation drives the DNA segregation, it is not "exerting force", but rather the addition of new polysomes is iteratively rectifying gaps being made by Brownian motion.

We apologize for the understandable confusion. In our picture, the polysomes and DNA (conceptually considered as small plectonemic segments) basically behave as dissolved particles. If these particles were noninteracting, they would simply mix. However, both polysomes and DNA segments are large enough to interact sterically. So as density increases, steric avoidance implies a reduced conformational entropy and thus a higher free energy per particle. We argue (based on Miangolarra et al. PNAS 2021 PMID: 34675077 and Xiang et al. Cell 2021 PMID: 34186018) that the demixing of polysomes and DNA segments occurs because DNA segments pack better with each other than they do with polysomes. This raises the free energy cost associated with DNA-polysome interactions compared to DNA-DNA interactions.  We model this effect by introducing a term in the free energy χ_np, which refer to as a repulsion between DNA and polysomes, though as explained above it arises from entropic effects. At realistic cellular densities of DNA and polysomes this repulsive interaction is strong enough to cause the DNA and polysomes to phase separate.

This same density-dependent free energy that causes phase separation can also give rise to forces, just in the way that a higher pressure on one side of a wall can give rise to a net force on the wall. Indeed, the “compaction force” we refer to is fundamentally an osmotic pressure difference. At some stages during nucleoid segregation, the region of the cell between nucleoids has a higher polysome concentration, and therefore a higher osmotic pressure, than the regions near the poles. This results in a net poleward force on the sister nucleoids that drives their migration toward the poles. This migration continues until the osmotic pressure equilibrates. Therefore, both phase separation (due to the steric repulsion described above) and nonequilibrium polysome production and degradation (which creates the initial accumulation of polysomes around midcell) are essential ingredients for nucleoid segregation.

This will be clarified in the revised text, with the support of additional simulation results.

The authors use polysome accumulation and phase separation to describe what is driving nucleoid segregation. Both terms are accurate, but it might help the less physically inclined reader to have one term, or have what each of these means explicitly defined at the start. I say this most especially in terms of "phase separation", as the currently huge momentum toward liquid-liquid interactions in biology causes the phrase "phase separation" to often evoke a number of wider (and less defined) phenomena and ideas that may not apply here. Thus, a simple clear definition at the start might help some readers.

Phase separation means that the DNA-polysome steric repulsion is strong enough to drive their demixing, which creates a compact nucleoid. As mentioned in a previous point, this effect is captured in the free energy by the χ_np term, which is an effective repulsion between DNA and polysomes, though as explained above it arises from entropic effects.

In the revised manuscript, we will illustrate this with our theoretical model by initializing a cell with a diffuse nucleoid and low polysome concentration. For the sake of simplicity, we assume that the cell does not elongate. We observe that the DNA-polysome steric repulsion is sufficient to compact the nucleoid and place it at mid-cell.

(4) Line 478. "Altogether, these results support the notion that ectopic polysome accumulation drives nucleoid dynamics". Is this right? Should it not read "results support the notion that ectopic polysome accumulation inhibits/redirects nucleoid dynamics"?

We think that this is correct; the ectopic polysome accumulation drives nucleoid dynamics. In our theoretical model, we can introduce polysome production at fixed sources to mimic the experiments where ectopic polysome production is achieved by high plasmid expression (Fig. 6). The model is able to recapitulate the two main phenotypes observed in experiments. These new simulation results will be added to the revised manuscript.

(5) It would be helpful to clarify what happens as the RplA-GFP signal decreases at midcell in Figure 1- is the signal then increasing in the less "dense" parts of the cell? That is, (a) are the polysomes at midcell redistributing throughout the cell? (b) is the total concentration of polysomes in the entire cell increasing over time?

It is a redistribution—the RplA-GFP signal remains constant in concentration from cell birth to division (Figure 1 – Figure Supplement 1E). This will be clarified in the revised text.

(6) Line 154. "Cell constriction contributed to the apparent depletion of ribosomal signal from the mid-cell region at the end of the cell division cycle (Figure 1B-C and Movie S1)" - It would be helpful if when cell constriction began and ended was indicated in Figures 1B and C.

Good idea. We will add markers to indicate the start of cell constriction. We will also indicate that cell birth and division correspond to the first and last images/timepoint in Fig. 1B and C, respectively.

(7) In Figure 7 they demonstrate that radial confinement is needed for longitudinal nucleoid segregation. It should be noted (and cited) that past experiments of Bacillus l-forms in microfluidic channels showed a clear requirement role for rod shape (and a given width) in the positing and the spacing of the nucleoids.

Wu et al, Nature Communications, 2020 . "Geometric principles underlying the proliferation of a model cell system" https://dx.doi.org/10.1038/s41467-020-17988-7

Good point. We will add this reference. Thank you.

(8) "The correlated variability in polysome and nucleoid patterning across cells suggests that the size of the polysome-depleted spaces helps determine where the chromosomal DNA is most concentrated along the cell length. This patterning is likely reinforced through the displacement of the polysomes away from the DNA dense region"

It should be noted this likely functions not just in one direction (polysomes dictating DNA location), but also in the reverse - as the footprint of compacted DNA should also exclude (and thus affect) the location of polysomes

We agree that the effects could go both ways at this early stage of the story. We will revise the text accordingly.  

(9) Line 159. Rifampicin is a transcription inhibitor that causes polysome depletion over time. This indicates that all ribosomal enrichments consist of polysomes and therefore will be referred to as polysome accumulations hereafter". Here and throughout this paper they use the term polysome, but cells also have monosomes (and 2 somes, etc). Rifampicin stops the assembly of all of these, and thus the loss of localization could occur from both. Thus, is it accurate to state that all transcription events occur in polysomes? Or are they grouping all of the n-somes into one group?

In the discussion, we noted that our term “polysomes” also includes monosomes for simplicity, but we agree that the term should have been defined much earlier. This will be done in the revised manuscript.

Thank you for the valuable comments and suggestions!

Reviewer #2 (Public review):

Summary:

The authors perform a remarkably comprehensive, rigorous, and extensive investigation into the spatiotemporal dynamics between ribosomal accumulation, nucleoid segregation, and cell division. Using detailed experimental characterization and rigorous physical models, they offer a compelling argument that nucleoid segregation rates are determined at least in part by the accumulation of ribosomes in the center of the cell, exerting a steric force to drive nucleoid segregation prior to cell division. This evolutionarily ingenious mechanism means cells can rely on ribosomal biogenesis as the sole determinant for the growth rate and cell division rate, avoiding the need for two separate 'sensors,' which would require careful coupling.

Terrific summary! Thank you for your positive assessment.

Strengths:

In terms of strengths; the paper is very well written, the data are of extremely high quality, and the work is of fundamental importance to the field of cell growth and division. This is an important and innovative discovery enabled through a combination of rigorous experimental work and innovative conceptual, statistical, and physical modeling.

Thank you!

Weaknesses:

In terms of weaknesses, I have three specific thoughts.

Firstly, my biggest question (and this may or may not be a bona fide weakness) is how unambiguously the authors can be sure their ribosomal labeling is reporting on polysomes, specifically. My reading of the work is that the loss of spatial density upon rifampicin treatment is used to infer that spatial density corresponds to polysomes, yet this feels like a relatively indirect way to get at this question, given rifampicin targets RNA polymerase and not translation. It would be good if a more direct way to confirm polysome dependence were possible.

The heterogeneity of ribosome distribution inside E. coli cells has been attributed to polysomes by many labs (PMID: 25056965, 38678067, 22624875, 31150626, 34186018, 10675340).  The attribution is also consistent with single-molecule tracking experiments showing that slow-moving ribosomes (polysomes) are excluded by the nucleoid whereas fast-diffusing ribosomes (free ribosomal subunits) are distributed throughout the cytoplasm (PMID: 25056965, 22624875).

Furthermore, inhibition of translation initiation with kasugamycin treatment, which decreases the pool of polysomes, results in a homogenization of ribosomes and expansion of the nucleoid (see Author response image 1). This further supports the rifampicin experiments. Given that the attribution of ribosome heterogeneity to polysomes is well accepted in the field, we would prefer to not include these kasugamycin data in the revised manuscript because long-term exposure to this drug leads to nucleoid re-compaction (PMID: 25250841 and PMID: 34186018). This secondary effect may possibly be due to a dysregulated increase in synthesis of naked rRNAs (PMID: 14460744, PMID: 2114400, and PMID: 2448483) or ribosome aggregation, which we are currently investigating.

Author response image 1.

Effects of kasugamycin treatment on the intracellular distribution of ribosomes and nucleoids. Representative single cell (CJW7323) growing in M9gluCAAT.  Kasugamycin (3 mg/mL) was added at time = 0 min. Show is the early response (0-30 min) to the drug characterized by the homogenization of the ribosomal RplA-GFP fluorescence and the expansion of the HupA-mCherry-labeled nucleoids. For each segmented cell, the RplA-GFP and HupA-mCherry signals were normalized by the average fluorescence.

Second, the authors invoke a phase separation model to explain the data, yet it is unclear whether there is any particular evidence supporting such a model, whether they can exclude simpler models of entanglement/local diffusion (and/or perhaps this is what is meant by phase separation?) and it's not clear if claiming phase separation offers any additional insight/predictive power/utility. I am OK with this being proposed as a hypothesis/idea/working model, and I agree the model is consistent with the data, BUT I also feel other models are consistent with the data. I also very much do not think that this specific aspect of the paper has any bearing on the paper's impact and importance.

We appreciate the reviewer’s comment, but the output of our reaction-diffusion model is a bona fide phase separation (spinodal decomposition). So, we feel that we need to use the term when reporting the modeling results. Inside the cell, the situation is more complicated. As the reviewer points out, there likely are entanglements (not considered in our model) and other important factors (please see our discussion on the model limitations). This said, we will revise our text to clarify our terms and proposed mechanism.

Finally, the writing and the figures are of extremely high quality, but the sheer volume of data here is potentially overwhelming. I wonder if there is any way for the authors to consider stripping down the text/figures to streamline things a bit? I also think it would be useful to include visually consistent schematics of the question/hypothesis/idea each of the figures is addressing to help keep readers on the same page as to what is going on in each figure. Again, there was no figure or section I felt was particularly unclear, but the sheer volume of text/data made reading this quite the mental endurance sport! I am completely guilty of this myself, so I don't think I have any super strong suggestions for how to fix this, but just something to consider.

We agree that there is a lot to digest. We will add schematics and a didactic simulation. We will also try to streamline the text.

Reviewer #3 (Public review):

Summary:

Papagiannakis et al. present a detailed study exploring the relationship between DNA/polysome phase separation and nucleoid segregation in Escherichia coli. Using a combination of experiments and modelling, the authors aim to link physical principles with biological processes to better understand nucleoid organisation and segregation during cell growth.

Strengths:

The authors have conducted a large number of experiments under different growth conditions and physiological perturbations (using antibiotics) to analyse the biophysical factors underlying the spatial organisation of nucleoids within growing E. coli cells. A simple model of ribosome-nucleoid segregation has been developed to explain the observations.

Weaknesses:

While the study addresses an important topic, several aspects of the modelling, assumptions, and claims warrant further consideration.

Thank you for your feedback. Please see below for a response to each concern. 

Major Concerns:

Oversimplification of Modelling Assumptions:

The model simplifies nucleoid organisation by focusing on the axial (long-axis) dimension of the cell while neglecting the radial dimension (cell width). While this approach simplifies the model, it fails to explain key experimental observations, such as:

(1) Inconsistencies with Experimental Evidence:

The simplified model presented in this study predicts that translation-inhibiting drugs like chloramphenicol would maintain separated nucleoids due to increased polysome fractions. However, experimental evidence shows the opposite-separated nucleoids condense into a single lobe post-treatment (Bakshi et al 2014), indicating limitations in the model's assumptions/predictions. For the nucleoids to coalesce into a single lobe, polysomes must cross the nucleoid zones via the radial shells around the nucleoid lobes.

We do not think that the results from chloramphenicol-treated cells are inconsistent with our model. Our proposed mechanism predicts that nucleoids will condense in the presence of chloramphenicol, consistent with experiments. It also predicts that nucleoids that were still relatively close at the time of chloramphenicol treatment could fuse if they eventually touched through diffusion (thermal fluctuation) to reduce their interaction with the polysomes and minimize their conformational energy. Fusion is, however, not expected for well-separated nucleoids since their diffusion is slow in the crowded cytoplasm. This is consistent with our experimental observations: In the presence of a growth-inhibitory concentration of chloramphenicol (70 μg/mL), nucleoids in relatively close proximity can fuse, but well-separated nucleoids condense and do not fuse. Since the growth rate inhibition is not immediate upon chloramphenicol treatment, many cells with well-separated condensed nucleoids divide during the first hour. As a result, the non-fusion phenotype is more obvious in non-dividing cells, achieved by pre-treating cells with the cell division inhibitor cephalexin (50μg/mL). In these polyploid elongated cells, well-separated nucleoids condensed but did not fuse, not even after an hour in the presence of chloramphenicol (as illustrated in Author response image 2).

In Bakshi et al, 2014, nucleoid fusion was shown for a single cell in which the sister nucleoids were relatively close to each other at the time of chloramphenicol treatment. Population statistics were provided for the relative length and width of the nucleoids, but not for the fusion events. So, it is unclear whether the illustrated fusion was universal or not. Also, we note that Bakshi et al (2014) used a chloramphenicol concentration of 300 μg/mL, which is 20-fold higher than the minimal inhibitory concentration for growth, compared to 70 μg/mL in our experiments.

Author response image 2.

Effects of chloramphenicol treatment on the intracellular distribution of ribosomes and nucleoids in non-dividing cells. Exponentially growing cells (M9glyCAAT at 30°C) were pre-treated with cephalexin for one hour before being spotted on an 1% agarose pad for time-lapse imaging. The agarose pad contained M9glyCAAT, cephalexin, and chloramphenicol.  (A) Phase contrast, RplA-GFP fluorescence and HupA-mCherry fluorescence images of a representative single cell. Three timepoints are shown, including the first image after spotting on the agarose pad (at 0 min), 30 minutes and one hour of chloramphenicol treatment. (B) One-dimensional profiles of the ribosomal (RplA-GFP) and nucleoid (HupA-mCherry) fluorescence from the cells shown in panel A. These intensity profiles correspond to the average fluorescence along the medial axis of the cell considering a 6-pixel region (0.4 μm) centered on the central line of the cell. The fluorescence intensity is plotted along the relative cell length, scaled from 0 to 100% between the two poles, illustrating the relative nucleoid length (L_DNA/L_cell) that was plotted by Bakshi et al in 2014 (PMID: 25250841).

(2) The peripheral localisation of nucleoids observed after A22 treatment in this study and others (e.g., Japaridze et al., 2020; Wu et al., 2019), which conflicts with the model's assumptions and predictions. The assumption of radial confinement would predict nucleoids to fill up the volume or ribosomes to go near the cell wall, not the nucleoid, as seen in the data.

The reviewer makes a good point that DNA attachment to the membrane through transertion likely contributes to the nucleoid being peripherally localized in A22 cells. We will revise the text to add this point. However, we do not think that this contradicts the proposed nucleoid segregation mechanism based on phase separation and out-of-equilibrium dynamics described in our model. On the contrary, by attaching the nucleoid to the cytoplasmic membrane along the cell width, transertion might help reduce the diffusion and thus exchange of polysomes across nucleoids. We will revise the text to discuss transertion over radial confinement.

(3) The radial compaction of the nucleoid upon rifampicin or chloramphenicol treatment, as reported by Bakshi et al. (2014) and Spahn et al. (2023), also contradicts the model's predictions. This is not expected if the nucleoid is already radially confined.

We originally evoked radial confinement to explain the observation that polysome accumulations do not equilibrate between DNA-free regions. We agree that transertion is an alternative explanation. Thank you for bringing it to our attention. However, please note that this does not contradict the model. In our view, it actually supports the 1D model by providing a reasonable explanation for the slow exchange of polysomes across DNA-free regions. The attachment of the nucleoid to the membrane along the cell width may act as diffusion barrier. We will revise the text and the title of the manuscript accordingly.

(4) Radial Distribution of Nucleoid and Ribosomal Shell:

The study does not account for well-documented features such as the membrane attachment of chromosomes and the ribosomal shell surrounding the nucleoid, observed in super-resolution studies (Bakshi et al., 2012; Sanamrad et al., 2014). These features are critical for understanding nucleoid dynamics, particularly under conditions of transcription-translation coupling or drug-induced detachment. Work by Yongren et al. (2014) has also shown that the radial organisation of the nucleoid is highly sensitive to growth and the multifork nature of DNA replication in bacteria.

We will discuss the membrane attachment. Please see the previous response.

The omission of organisation in the radial dimension and the entropic effects it entails, such as ribosome localisation near the membrane and nucleoid centralisation in expanded cells, undermines the model's explanatory power and predictive ability. Some observations have been previously explained by the membrane attachment of nucleoids (a hypothesis proposed by Rabinovitch et al., 2003, and supported by experiments from Bakshi et al., 2014, and recent super-resolution measurements by Spahn et al.).

We agree—we will add a discussion about membrane attachment in the radial dimension. See previous responses.

Ignoring the radial dimension and membrane attachment of nucleoid (which might coordinate cell growth with nucleoid expansion and segregation) presents a simplistic but potentially misleading picture of the underlying factors.

As mentioned above, we will discuss membrane attachment in the revised manuscript.

This reviewer suggests that the authors consider an alternative mechanism, supported by strong experimental evidence, as a potential explanation for the observed phenomena:

Nucleoids may transiently attach to the cell membrane, possibly through transertion, allowing for coordinated increases in nucleoid volume and length alongside cell growth and DNA replication. Polysomes likely occupy cellular spaces devoid of the nucleoid, contributing to nucleoid compaction due to mutual exclusion effects. After the nucleoids separate following ter separation, axial expansion of the cell membrane could lead to their spatial separation.

This “membrane attachment/cell elongation” model is reminiscent to the hypothesis proposed by Jacob et al in 1963 (doi:10.1101/SQB.1963.028.01.048). There are several lines of evidence arguing against it as the major driver of nucleoid segregation:

(Below is a slightly modified version of our response to a comment from Reviewer 1—see page 3)

(1) For this alternative model to work, axial membrane expansion (i.e., cell elongation) would have to be localized at the middle of the splitting nucleoids (i.e., midcell position for slow growth and ¼ and ¾ cell positions for fast growth) to create a directional motion. To our knowledge, there is no evidence of such localized membrane incorporation.  Furthermore, even if membrane growth was localized at the right places, the fluidity of the cytoplasmic membrane (PMID: 6996724, 20159151, 24735432, 27705775) would be problematic. To go around this fluidity issue, one could potentially evoke a potential connection to the rigid peptidoglycan, but then again, peptidoglycan growth would have to be localized at the middle of the splitting nucleoid to “push” the sister nucleoid apart from each other. However, peptidoglycan growth is dispersed prior to cell constriction (PMID: 35705811, 36097171, 2656655).

(2) Even if we ignore the aforementioned caveats, Paul Wiggins’s group ruled out the cell elongation/transertion model by showing that the rate of cell elongation is slower than the rate of chromosome segregation (PMID: 23775792). In the revised manuscript, we will provide additional data showing that the cell elongation rate is indeed slower than the nucleoid segregation rate.

(3) Furthermore, our correlation analysis comparing the rate of nucleoid segregation to the rate of either cell elongation or polysome accumulation argues that polysome accumulation plays a larger role than cell elongation in nucleoid segregation. These data were already shown in the original manuscript (Figure 1I and Figure 1 – figure supplement 3) but were not highlighted in this context. We will revise the text to clarify this point.

(4) The membrane attachment/cell elongation model does not explain the nucleoid asymmetries described in our paper (Figure 3), whereas they can be recapitulated by our model.

(5) The cell elongation/transertion model cannot predict the aberrant nucleoid dynamics observed when chromosomal expression is largely redirected to plasmid expression. In the revised manuscript, we will add simulation results showing that these nucleoid dynamics are predicted by our model.

In line of these arguments, we do not believe that a mechanism based on membrane attachment and cell elongation is the major driver of nucleoid segregations. However, we do believe that it may play a complementary role (see “Nucleoid segregation likely involves multiple factors” in the Discussion). We will revise this section to clarify our thoughts and mention the potential role of transertion.

Incorporating this perspective into the discussion or future iterations of the model may provide a more comprehensive framework that aligns with the experimental observations in this study and previous work.

As noted above, we will revise the text to mention about transertion.

Simplification of Ribosome States:

Combining monomeric and translating ribosomes into a single 'polysome' category may overlook spatial variations in these states, particularly during ribosome accumulation at the mid-cell. Without validating uniform mRNA distribution or conducting experimental controls such as FRAP or single-molecule measurements to estimate the proportions of ribosome states based on diffusion, this assumption remains speculative.

Indeed, for simplicity, we adopt an average description of all polysomes with an average diffusion coefficient and interaction parameters, which is sufficient for capturing the fundamental mechanism underlying nucleoid segregation. To illustrate that considering multiple polysome species does not change the physical picture, we consider an extension of our model, which contains three polysome species, each with a different diffusion coefficient (D<SUB>P</SUB> = 0.018, 0.023, or 0.028 μm²/s), reflecting that polysomes with more ribosomes will have a lower diffusion coefficient. Simulation of this model reveals that the different polysome species have essentially the same concentration distribution, suggesting that the average description in our minimal model is sufficient for our purposes. We will present these new simulation results in the revised manuscript.

Author response:

eLife assessment

This study provides valuable information on the mechanism of PepT2 through enhanced-sampling molecular dynamics, backed by cell-based assays, highlighting the importance of protonation of selected residues for the function of a proton-coupled oligopeptide transporter (hsPepT2). The molecular dynamics approaches are convincing, but with limitations that could be addressed in the manuscript, including lack of incorporation of a protonation coordinate in the free energy landscape, possibility of protonation of the substrate, errors with the chosen constant pH MD method for membrane proteins, dismissal of hysteresis emerging from the MEMENTO method, and the likelihood of other residues being affected by peptide binding. Some changes to the presentation could be considered, including a better description of pKa calculations and the inclusion of error bars in all PMFs. Overall, the findings will appeal to structural biologists, biochemists, and biophysicists studying membrane transporters.

We would like to express our gratitude to the reviewers for providing their feedback on our manuscript, and also for recognising the variety of computational methods employed, the amount of sampling collected and the experimental validation undertaken. Following the individual reviewer comments, as addressed point-by-point below, we will shortly prepare a revised version of this paper. Intended changes to the revised manuscript are marked up in bold font in the detailed responses below, but before that we address some of the comments made above in the general assessment:

• “lack of incorporation of a protonation coordinate in the free energy landscape”. We acknowledge that of course it would be highly desirable to treat protonation state changes explicitly and fully coupled to conformational changes. However, at this point in time, evaluating such a free energy landscape is not computationally feasible (especially considering that the non-reactive approach taken here already amounts to almost 1ms of total sampling time). Previous reports in the literature tend to focus on either simpler systems or a reduced subset of a larger problem. As we were trying to obtain information on the whole transport cycle, we decided to focus here on non-reactive methods.

• “possibility of protonation of the substrate”. The reviewers are correct in pointing out this possibility, which we had not discussed explicitly in our manuscript. Briefly, while we describe a mechanism in which protonation of only protein residues (with an unprotonated ligand) can account for driving all the necessary conformational changes of the transport cycle, there is some evidence for a further intermediate protonation site in our data (as we commented on in the first version of the manuscript as well), which may or may not be the substrate itself. A future explicit treatment of the proton movements through the transporter, when it will become computationally tractable to do so, will have to include the substrate as a possible protonation site; for the present moment, we will amend our discussion to alert the reader to the possibility that the substrate could be an intermediate to proton transport. This has repercussions for our study of the E56 pKa value, where – if protons reside with a significant population at the substrate C-terminus – our calculated shift in pKa upon substrate binding could be an overestimate, although we would qualitatively expect the direction of shift to be unaffected. However, we also anticipate that treating this potential coupling explicitly would make convergence of any CpHMD calculation impractical to achieve and thus it may be the case that for now only a semi-quantitative conclusion is all that can be obtained.

• “errors with the chosen constant pH MD method for membrane proteins”. We acknowledge that – as reviewer #1 has reminded us – the AMBER implementation of hybrid-solvent CpHMD is not rigorous for membrane proteins, and as such we will add a cautionary note to our paper. We will also explain how the use of the ABFE thermodynamic cycle calculations helps to validate the CpHMD results in a completely orthogonal manner (we will promote this validation which was in the supplementary figures into the main text in the revised version). We therefore remain reasonably confident in the results presented with regards to the reported pKa shift of E56 upon substrate binding, and suggest that if the impact of neglecting the membrane in the implicit-solvent stage of CpHMD is significant, then there is likely an error cancellation when considering shifts induced by the incoming substrate.

• “dismissal of hysteresis emerging from the MEMENTO method”. We have shown in our method design paper how the use of the MEMENTO method drastically reduces hysteresis compared to steered MD and metadynamics for path generation, and find this improvement again for PepT2 in this study. We will address reviewer #3’s concern about our presentation on this point by revising our introduction of the MEMENTO method, as detailed in the response below.

• “the likelihood of other residues being affected by peptide binding”. In this study, we have investigated in detail the involvement of several residues in proton-coupled di-peptide transport by PepT2. Short of the potential intermediate protonation site mentioned above, the set of residues we investigate form a minimal set of sorts within which the important driving forces of alternating access can be rationalised. We have not investigated in substantial detail here the residues involved in holding the peptide in the binding site, as they are well studied in the literature and ligand promiscuity is not the problem of interest here. It remains entirely possible that further processes contribute to the mechanism of driving conformational changes by involving other residues not considered in this paper. We will make our speculation that an ensemble of different processes may be contributing simultaneously more explicit in our revision, but do not believe any of our conclusions would be affected by this.

As for the additional suggested changes in presentation, we will provide the requested details on the CpHMD analysis. Furthermore, we will use the convergence data presented separately in figures S12 and S16 to include error bars on our 1D-reprojections of the 2D-PMFs in figures 3, 4 and 5. (Note that we will opt to not do so in figures S10 and S15 which collate all 1D PMF reprojections for the OCC ↔ OF and OCC ↔ IF transitions in single reference plots, respectively, to avoid overcrowding those necessarily busy figures). We are also changing the colours schemes of these plots in our revision to improve accessibility.

Reviewer #1 (Public Review):

The authors have performed all-atom MD simulations to study the working mechanism of hsPepT2. It is widely accepted that conformational transitions of proton-coupled oligopeptide transporters (POTs) are linked with gating hydrogen bonds and salt bridges involving protonatable residues, whose protonation triggers gate openings. Through unbiased MD simulations, the authors identified extra-cellular (H87 and D342) and intra-cellular (E53 and E622) triggers. The authors then validated these triggers using free energy calculations (FECs) and assessed the engagement of the substrate (Ala-Phe dipeptide). The linkage of substrate release with the protonation of the ExxER motif (E53 and E56) was confirmed using constant-pH molecular dynamics (CpHMD) simulations and cellbased transport assays. An alternating-access mechanism was proposed. The study was largely conducted properly, and the paper was well-organized. However, I have a couple of concerns for the authors to consider addressing.

We would like to note here that it may be slightly misleading to the reader to state that “The linkage of substrate release with the protonation of the ExxER motif (E53 and E56) was confirmed using constant-pH molecular dynamics (CpHMD) simulations and cell-based transport assays.” The cellbased transport assays confirmed the importance of the extracellular gating trigger residues H87, S321 and D342 (as mentioned in the preceding sentence), not of the substrate-protonation link as this line might be understood to suggest.

(1) As a proton-coupled membrane protein, the conformational dynamics of hsPepT2 are closely coupled to protonation events of gating residues. Instead of using semi-reactive methods like CpHMD or reactive methods such as reactive MD, where the coupling is accounted for, the authors opted for extensive non-reactive regular MD simulations to explore this coupling. Note that I am not criticizing the choice of methods, and I think those regular MD simulations were well-designed and conducted. But I do have two concerns.

a) Ideally, proton-coupled conformational transitions should be modelled using a free energy landscape with two or more reaction coordinates (or CVs), with one describing the protonation event and the other describing the conformational transitions. The minimum free energy path then illustrates the reaction progress, such as OCC/H87D342- → OCC/H87HD342H → OF/H87HD342H as displayed in Figure 3.

We concur with the reviewer that the ideal way of describing the processes studied in our paper would be as a higher-dimensional free energy landscapes obtained from a simulation method that can explicitly model proton-transfer processes. Indeed, it would have been particularly interesting and potentially informative with regards to the movement of protons down into the transporter in the OF → OCC → IF sequence of transitions. As we note in our discussion on the H87→E56 proton transfer:

“This could be investigated using reactive MD or QM/MM simulations (both approaches have been employed for other protonation steps of prokaryotic peptide transporters, see Parker et al. (2017) and Li et al. (2022)). However, the putative path is very long (≈ 1.7 nm between H87 and E56) and may or may not involve a large number of intermediate protonatable residues, in addition to binding site water. While such an investigation is possible in principle, it is beyond the scope of the present study.”

Where even sampling the proton transfer step itself in an essentially static protein conformation would be pushing the boundaries of what has been achieved in the field, we believe that considering the current state-of-the-art, a fully coupled investigation of large-scale conformational changes and proton-transfer reaction is not yet feasible in a realistic/practical time frame. We also note this limitation already when we say that:

“The question of whether proton binding happens in OCC or OF warrants further investigation, and indeed the co-existence of several mechanisms may be plausible here”.

Nonetheless, we are actively exploring approaches to treat uptake and movement of protons explicitly for future work.

In our revision, we will expand on our discussion of the reasoning behind employing a nonreactive approach and the limitations that imposes on what questions can be answered in this study.

Without including the protonation as a CV, the authors tried to model the free energy changes from multiple FECs using different charge states of H87 and D342. This is a practical workaround, and the conclusion drawn (the OCC→ OF transition is downhill with protonated H87 and D342) seems valid. However, I don't think the OF states with different charge states (OF/H87D342-, OF/H87HD342-, OF/H87D342H, and OF/H87HD342H) are equally stable, as plotted in Figure 3b. The concern extends to other cases like Figures 4b, S7, S10, S12, S15, and S16. While it may be appropriate to match all four OF states in the free energy plot for comparison purposes, the authors should clarify this to ensure readers are not misled.

The reviewer is correct in their assessment that the aligning of PMFs in these figures is arbitrary; no relative free energies of the PMFs to each other can be estimated without explicit free energy calculations at least of protonation events at the end state basins. The PMFs in our figures are merely superimposed for illustrating the differences in shape between the obtained profiles in each condition, as discussed in the text, and we will make this clear in the appropriate figure captions in our revision.

b) Regarding the substrate impact, it appears that the authors assumed fixed protonation states. I am afraid this is not necessarily the case. Variations in PepT2 stoichiometry suggest that substrates likely participate in proton transport, like the Phe-Ala (2:1) and Phe-Gln (1:1) dipeptides mentioned in the introduction. And it is not rigorous to assume that the N- and C-termini of a peptide do not protonate/deprotonate when transported. I think the authors should explicitly state that the current work and the proposed mechanism (Figure 8) are based on the assumption that the substrates do not uptake/release proton(s).

This is indeed an assumption inherent in the current work. While we do “speculate that the proton movement processes may happen as an ensemble of different mechanisms, and potentially occur contemporaneously with the conformational change” we do not in the current version indicate explicitly that this may involve the substrate. We will make clear the assumption and this possibility in the revised version of our paper. Indeed, as we discuss, there is some evidence in our PMFs of an additional protonation site not considered thus far, which may or may not be the substrate. We will make note of this point in the revised manuscript.

As for what information can be drawn from the given experimental stoichiometries, we note in our paper that “a 2:1 stoichiometry was reported for the neutral di-peptide D-Phe-L-Ala and 3:1 for anionic D-Phe-L-Glu. (Chen et al., 1999) Alternatively, Fei et al. (1999) have found 1:1 stoichiometries for either of D-Phe-L-Gln (neutral), D-Phe-L-Glu (anionic), and D-Phe-L-Lys (cationic).”

We do not assume that it is our place to arbit among the apparent discrepancies in the experimental data here, although we believe that our assumed 2:1 stoichiometry is additionally “motivated also by our computational results that indicate distinct and additive roles played by two protons in the conformational cycle mechanism”.

(2) I have more serious concerns about the CpHMD employed in the study.

a) The CpHMD in AMBER is not rigorous for membrane simulations. The underlying generalized Born model fails to consider the membrane environment when updating charge states. In other words, the CpHMD places a membrane protein in a water environment to judge if changes in charge states are energetically favorable. While this might not be a big issue for peripheral residues of membrane proteins, it is likely unphysical for internal residues like the ExxER motif. As I recall, the developers have never used the method to study membrane proteins themselves. The only CpHMD variant suitable for membrane proteins is the membrane-enabled hybrid-solvent CpHMD in CHARMM. While I do not expect the authors to redo their CpHMD simulations, I do hope the authors recognize the limitations of their method.

We will discuss the limitations of the AMBER CpHMD implementation in the revised version. However, despite that, we believe we have in fact provided sufficient grounds for our conclusion that substrate binding affects ExxER motif protonation in the following way:

In addition to CpHMD simulations, we establish the same effect via ABFE calculations, where the substrate affinity is different at the E56 deprotonated vs protonated protein. This is currently figure S20, though in the revised version we will move this piece of validation into a new panel of figure 6 in the main text, since it becomes more important with the CpHMD membrane problem in mind. Since the ABFE calculations are conducted with an all-atom representation of the lipids and the thermodynamic cycle closes well, it would appear that if the chosen CpHMD method has a systematic error of significant magnitude for this particular membrane protein system, there may be the benefit of error cancellation. While the calculated absolute pKa values may not be reliable, the difference made by substrate binding appears to be so, as judged by the orthogonal ABFE technique.

Although the reviewer does “not expect the authors to redo their CpHMD simulations”, we consider that it may be helpful to the reader to share in this response some results from trials using the continuous, all-atom constant pH implementation that has recently become available in GROMACS (Aho et al 2022, https://pubs.acs.org/doi/10.1021/acs.jctc.2c00516) and can be used rigorously with membrane proteins, given its all-atom lipid representation.

Unfortunately, when trying to titrate E56 in this CpHMD implementation, we found few protonationstate transitions taking place, and the system often got stuck in protonation state–local conformation coupled minima (which need to interconvert through rearrangements of the salt bridge network involving slow side-chain dihedral rotations in E53, E56 and R57). Author response image 1 shows this for the apo OF state, Author response image 2 shows how noisy attempts at pKa estimation from this data turn out to be, necessitating the use of a hybrid-solvent method.

Author response image 1.

All-atom CpHMD simulations of apo-OF PepT2. Red indicates protonated E56, blue is deprotonated.

Author response image 2.

Difficulty in calculating the E56 pKa value from the noisy all-atom CpHMD data shown in Author response image 1

b) It appears that the authors did not make the substrate (Ala-Phe dipeptide) protonatable in holosimulations. This oversight prevents a complete representation of ligand-induced protonation events, particularly given that the substrate ion pairs with hsPepT2 through its N- & C-termini. I believe it would be valuable for the authors to acknowledge this potential limitation.

In this study, we implicitly assumed from the outset that the substrate does not get protonated, which – as by way of response to the comment above – we will acknowledge explicitly in revision. This potential limitation for the available mechanisms for proton transfer also applies to our investigation of the ExxER protonation states. In particular, a semi-grand canonical ensemble that takes into account the possibility of substrate C-terminus protonation may also sample states in which the substrate is protonated and oriented away from R57, thus leaving the ExxER salt bridge network in an apo-like state. The consequence would be that while the direction of shift in E56 pKa value will be the same, our CpHMD may overestimate its magnitude. It would thus be interesting to make the C-terminus protonatable for obtaining better quantitative estimates of the E56 pKa shift (as is indeed true in general for any other protein protonatable residue, though the effects are usually assumed to be negligible). We do note, however, that convergence of the CpHMD simulations would be much harder if the slow degree of freedom of substrate reorientation (which in our experience takes 10s to 100s of ns in this binding pocket) needs to be implicitly equilibrated upon protonation state transitions. We will discuss such considerations in the revision.

Reviewer #2 (Public Review):

This is an interesting manuscript that describes a series of molecular dynamics studies on the peptide transporter PepT2 (SLC15A2). They examine, in particular, the effect on the transport cycle of protonation of various charged amino acids within the protein. They then validate their conclusions by mutating two of the residues that they predict to be critical for transport in cell-based transport assays. The study suggests a series of protonation steps that are necessary for transport to occur in Petp2. Comparison with bacterial proteins from the same family shows that while the overall architecture of the proteins and likely mechanism are similar, the residues involved in the mechanism may differ.

Strengths:

This is an interesting and rigorous study that uses various state-of-the-art molecular dynamics techniques to dissect the transport cycle of PepT2 with nearly 1ms of sampling. It gives insight into the transport mechanism, investigating how the protonation of selected residues can alter the energetic barriers between various states of the transport cycle. The authors have, in general, been very careful in their interpretation of the data.

Weaknesses:

Interestingly, they suggest that there is an additional protonation event that may take place as the protein goes from occluded to inward-facing but they have not identified this residue.

We have indeed suggested that there may be an additional protonation site involved in the conformational cycle that we have not been able to capture, which – as we discuss in our paper – might be indicated by the shapes of the OCC ↔ IF PMFs given in Figure S15. One possibility is for this to be the substrate itself (see the response to reviewer #1 above) though within the scope of this study the precise pathway by which protons move down the transporter and the exact ordering of conformational change and proton transfer reactions remains a (partially) open question. We acknowledge this and denote it with question marks in the mechanistic overview we give in Figure 8, and also “speculate that the proton movement processes may happen as an ensemble of different mechanisms, and potentially occur contemporaneously with the conformational change”.

Some things are a little unclear. For instance, where does the state that they have defined as occluded sit on the diagram in Figure 1a? - is it truly the occluded state as shown on the diagram or does it tend to inward- or outward-facing?

Figure 1a is a simple schematic overview intended to show which structures of PepT2 homologues are available to use in simulations. This was not meant to be a quantitative classification of states. Nonetheless, we can note that the OCC state we derived has extra- and intracellular gate opening distances (as measured by the simple CVs defined in the methods and illustrated in Figure 2a) that indicate full gate closure at both sides. In particular, although it was derived from the IF state via biased sampling, the intracellular gate opening distance in the OCC state used for our conformational change enhanced sampling was comparable to that of the OF state (ie, full closure of the gate), see Figure S2b and the grey bars therein. Therefore, we would schematically classify the OCC state to lie at the center of the diagram in Figure 1a. Furthermore, it is largely stable over triplicates of 1 μslong unbiased MD, where in 2/3 replicates the gates remain stable, and the remaining replicate there is partial opening of the intracellular gate (as shown in Figure 2 b/c under the “apo standard” condition). We comment on this in the main text by saying that “The intracellular gate, by contrast, is more flexible than the extracellular gate even in the apo, standard protonation state”, and link it to the lower barrier for transition to IF than to OF. We did this by saying that “As for the OCC↔OF transitions, these results explain the behaviour we had previously observed in the unbiased MD of Figure 2c.” We acknowledge this was not sufficiently clear and will add details to the latter sentence in revision to help clarify better the nature of the occluded state.

The pKa calculations and their interpretation are a bit unclear. Firstly, it is unclear whether they are using all the data in the calculations of the histograms, or just selected data and if so on what basis was this selection done. Secondly, they dismiss the pKa calculations of E53 in the outward-facing form as not being affected by peptide binding but say that E56 is when there seems to be a similar change in profile in the histograms.

In our manuscript, we have provided two distinct analyses of the raw CpHMD data. Firstly, we analysed the data by the replicates in which our simulations were conducted (Figure 6, shown as bar plots with mean from triplicates +/- standard deviation), where we found that only the effect on E56 protonation was distinct as lying beyond the combined error bars. This analysis uses the full amount of sampling conducted for each replicate. However, since we found that the range of pKa values estimated from 10ns/window chunks was larger than the error bars obtained from the replicate analysis (Figures S17 and S18), we sought to verify our conclusion by pooling all chunk estimates and plotting histograms (Figure S19). We recover from those the effect of substrate binding on the E56 protonation state on both the OF and OCC states. However, as the reviewer has pointed out (something we did not discuss in our original manuscript), there is a shift in the pKa of E53 of the OF state only. In fact, the trend is also apparent in the replicate-based analysis of Figure 6, though here the larger error bars overlap. In our revision, we will add more details of these analyses for clarity (including more detailed figure captions regarding the data used in Figure 6) as well as a discussion of the partial effect on the E53 pKa value.

We do not believe, however, that our key conclusions are negatively affected. If anything, a further effect on the E53 pKa which we had not previously commented on (since we saw the evidence as weaker, pertaining to only one conformational state) would strengthen the case for an involvement of the ExxER motif in ligand coupling.

Reviewer #3 (Public Review):

Summary:

Lichtinger et al. have used an extensive set of molecular dynamics (MD) simulations to study the conformational dynamics and transport cycle of an important member of the proton-coupled oligopeptide transporters (POTs), namely SLC15A2 or PepT2. This protein is one of the most wellstudied mammalian POT transporters that provides a good model with enough insight and structural information to be studied computationally using advanced enhanced sampling methods employed in this work. The authors have used microsecond-level MD simulations, constant-PH MD, and alchemical binding free energy calculations along with cell-based transport assay measurements; however, the most important part of this work is the use of enhanced sampling techniques to study the conformational dynamics of PepT2 under different conditions.

The study attempts to identify links between conformational dynamics and chemical events such as proton binding, ligand-protein interactions, and intramolecular interactions. The ultimate goal is of course to understand the proton-coupled peptide and drug transport by PepT2 and homologous transporters in the solute carrier family.

Some of the key results include:

(1) Protonation of H87 and D342 initiate the occluded (Occ) to the outward-facing (OF) state transition.

(2) In the OF state, through engaging R57, substrate entry increases the pKa value of E56 and thermodynamically facilitates the movement of protons further down.

(3) E622 is not only essential for peptide recognition but also its protonation facilitates substrate release and contributes to the intracellular gate opening. In addition, cell-based transport assays show that mutation of residues such as H87 and D342 significantly decreases transport activity as expected from simulations.

Strengths:

(1) This is an extensive MD-based study of PepT2, which is beyond the typical MD studies both in terms of the sheer volume of simulations as well as the advanced methodology used. The authors have not limited themselves to one approach and have appropriately combined equilibrium MD with alchemical free energy calculations, constant-pH MD, and geometry-based free energy calculations. Each of these 4 methods provides a unique insight regarding the transport mechanism of PepT2.

(2) The authors have not limited themselves to computational work and have performed experiments as well. The cell-based transport assays clearly establish the importance of the residues that have been identified as significant contributors to the transport mechanism using simulations.

(3) The conclusions made based on the simulations are mostly convincing and provide useful information regarding the proton pathway and the role of important residues in proton binding, protein-ligand interaction, and conformational changes.

Weaknesses:

(1) Some of the statements made in the manuscript are not convincing and do not abide by the standards that are mostly followed in the manuscript. For instance, on page 4, it is stated that "the K64-D317 interaction is formed in only ≈ 70% of MD frames and therefore is unlikely to contribute much to extracellular gate stability." I do not agree that 70% is negligible. Particularly, Figure S3 does not include the time series so it is not clear whether the 30% of the time where the salt bridge is broken is in the beginning or the end of simulations. For instance, it is likely that the salt bridge is not initially present and then it forms very strongly. Of course, this is just one possible scenario but the point is that Figure S3 does not rule out the possibility of a significant role for the K64-D317 salt bridge.

The reviewer is right to point out that the statement and Figure S3 as they stand do not adequately support our decision to exclude the K64-D317 salt-bridge in our further investigations. The violin plot shown in Figure S3, visualised as pooled data from unbiased 1 μs triplicates, does indeed not rule out a scenario where the salt bridge only formed late in our simulations (or only in some replicates), but then is stable. Therefore, in our revision, we will include the appropriate time-series of the salt bridge distances, showing how K64-D317 is initially stable but then falls apart in replicate 1, and is transiently formed and disengaged across the trajectories in replicates 2 and 3. We will also remake the data for this plot as we discovered a bug in the relevant analysis script that meant the D170-K642 distance was not calculated accurately. The results are however almost identical, and our conclusions remain.

(2) Similarly, on page 4, it is stated that "whether by protonation or mutation - the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed (Figure S5)." I do not agree with this assessment. The authors need to be aware of the limitations of this approach. Consider "WT H87-prot" and "D342A H87-prot": when D342 residue is mutated, in one out of 3 simulations, we see the opening of the gate within 1 us. When D342 residue is not mutated we do not see the opening in any of the 3 simulations within 1 us. It is quite likely that if rather than 3 we have 10 simulations or rather than 1 us we have 10 us simulations, the 0/3 to 1/3 changes significantly. I do not find this argument and conclusion compelling at all.

If the conclusions were based on that alone, then we would agree. However, this section of work covers merely the observations of the initial unbiased simulations which we go on to test/explore with enhanced sampling in the rest of the paper, and which then lead us to the eventual conclusions.

Figure S5 shows the results from triplicate 1 μs-long trajectories as violin-plot histograms of the extracellular gate opening distance, also indicating the first and final frames of the trajectories as connected by an arrow for orientation – a format we chose for intuitively comparing 48 trajectories in one plot. The reviewer reads the plot correctly when they analyse the “WT H87-prot” vs “D342A H87-prot” conditions. In the former case, no spontaneous opening in unbiased MD is taking place, whereas when D342 is mutated to alanine in addition to H87 protonation, we see spontaneous transition in 1 out of 3 replicates. However, the reviewer does not seem to interpret the statement in question in our paper (“the extracellular gate only opens spontaneously when both the H87 interaction network and D342-R206 are perturbed”) in the way we intended it to be understood. We merely want to note here a correlation in the unbiased dataset we collected at this stage, and indeed the one spontaneous opening in the case comparison picked out by the reviewer is in the condition where both the H87 interaction network and D342-R206 are perturbed. In noting this we do not intend to make statistically significant statements from the limited dataset. Instead, we write that “these simulations show a large amount of stochasticity and drawing clean conclusions from the data is difficult”. We do however stand by our assessment that from this limited data we can “already appreciate a possible mechanism where protons move down the transporter pore” – a hypothesis we investigate more rigorously with enhanced sampling in the rest of the paper. We will revise the section in question to make clearer that the unbiased MD is only meant to give an initial hypothesis here to be investigated in more detail in the following sections. In doing so, we will also incorporate, as we had not done before, the case (not picked out by the reviewer here but concerning the same figure) of S321A & H87 prot. In the third replicate, this shows partial gate opening towards the end of the unbiased trajectory (despite D342 not being affected), highlighting further the stochastic nature that makes even clear correlative conclusions difficult to draw.

(3) While the MEMENTO methodology is novel and interesting, the method is presented as flawless in the manuscript, which is not true at all. It is stated on Page 5 with regards to the path generated by MEMENTO that "These paths are then by definition non-hysteretic." I think this is too big of a claim to say the paths generated by MEMENTO are non-hysteretic by definition. This claim is not even mentioned in the original MEMENTO paper. What is mentioned is that linear interpolation generates a hysteresis-free path by definition. There are two important problems here: (a) MEMENTO uses the linear interpolation as an initial step but modifies the intermediates significantly later so they are no longer linearly interpolated structures and thus the path is no longer hysteresisfree; (b) a more serious problem is the attribution of by-definition hysteresis-free features to the linearly interpolated states. This is based on conflating the hysteresis-free and unique concepts. The hysteresis in MD-based enhanced sampling is related to the presence of barriers in orthogonal space. For instance, one may use a non-linear interpolation of any type and get a unique pathway, which could be substantially different from the one coming from the linear interpolation. None of these paths will be hysteresis-free necessarily once subjected to MD-based enhanced sampling techniques.

We certainly do not intend to claim that the MEMENTO method is flawless. The concern the reviewer raises around the statement "These paths are then by definition non-hysteretic" is perhaps best addressed by a clarification of the language used and considering how MEMENTO is applied in this work.

Hysteresis in the most general sense denotes the dependence of a system on its history, or – more specifically – the lagging behind of the system state with regards to some physical driver (for example the external field in magnetism, whence the term originates). In the context of biased MD and enhanced sampling, hysteresis commonly denotes the phenomenon where a path created by a biased dynamics method along a certain collective variable lags behind in phase space in slow orthogonal degrees of freedom (see Figure 1 in Lichtinger and Biggin 2023, https://doi.org/10.1021/acs.jctc.3c00140). When used to generate free energy profiles, this can manifest as starting state bias, where the conformational state that was used to seed the biased dynamics appears lower in free energy than alternative states. Figure S6 shows this effect on the PepT2 system for both steered MD (heavy atom RMSD CV) + umbrella sampling (tip CV) and metadynamics (tip CV). There is, in essence, a coupled problem: without an appropriate CV (which we did not have to start with here), path generation that is required for enhanced sampling displays hysteresis, but the refinement of CVs is only feasible when paths connecting the true phase space basins of the two conformations are available. MEMENTO helps solve this issue by reconstructing protein conformations along morphing paths which perform much better than steered MD paths with respect to giving consistent free energy profiles (see Figure S7 and the validation cases in the MEMENTO paper), even if the same CV is used in umbrella sampling.

There are still differences between replicates in those PMFs, indicating slow conformational flexibility propagated from end-state sampling through MEMENTO. We use this to refine the CVs further with dimensionality reduction (see the Method section and Figure S8), before moving to 2D-umbrella sampling (figure 3). Here, we think, the reviewer’s point seems to bear. The MEMENTO paths are ‘non-hysteretic by definition’ with respect to given end states in the sense that they connect (by definition) the correct conformations at both end-states (unlike steered MD), which in enhanced sampling manifests as the absence of the strong starting-state bias we had previously observed (Figure S7 vs S6). They are not, however, hysteresis-free with regards to how representative of the end-state conformational flexibility the structures given to MEMENTO really were, which is where the iterative CV design and combination of several MEMENTO paths in 2D-PMFs comes in.

We also cannot make a direct claim about whether in the transition region the MEMENTO paths might be separated from the true (lower free energy) transition paths by slow orthogonal degrees of freedom, which may conceivably result in overestimated barrier heights separating two free energy basins. We cannot guarantee that this is not the case, but neither in our MEMENTO validation examples nor in this work have we encountered any indications of a problem here.

We hope that the reviewer will be satisfied by our revision, where we will replace the wording in question by a statement that the MEMENTO paths do not suffer from hysteresis that is otherwise incurred as a consequence of not reaching the correct target state in the biased run (in some orthogonal degrees of freedom).

Author Response

Joint Public Review

The molecular composition of synaptic vesicles (SVs) has been defined in substantial detail, but the function of many SV-resident proteins are still unknown. The present study focused on one such protein, the 'orphan' SV-resident transporter SLC6A17. By utilizing sophisticated and extensive mouse genetics and behavioral experiments, the authors provide convincing support for the notion that certain SLC6A17 variants cause intellectual disability (ID) in humans carrying such genetic variations. This is an important and novel finding. Furthermore, the authors propose, based on LCMS analyses of isolated SVs, that SLC6A17 is responsible for glutamine (Gln) transport into SVs, leading to the provocative idea that Gln functions as a neurotransmitter and that deficits in Gln transport into SVs by SLC6A17 represents a key pathogenetic mechanism in human ID patients carrying variants of the SLC6A17 gene.

This latter aspect of the present paper is not adequately supported by the experimental evidence so that the main conceptual claims of the study appear insufficiently justified at this juncture. Key weaknesses are as follows:

A) Detection of Gln, along with classical neurotransmitters such as glutamate, GABA, or ACh, in isolated SV fractions does not prove that Gln is transported into SVs by active transport. Gln is quite abundant in extracellular compartments. Its appearance in SV samples can therefore also be explained by trapping in SVs during endocytosis, presence in other - contaminating - organelles, binding to membrane surfaces, and other processes. Direct assays of Gln uptake into SVs, which have the potential to stringently test key postulates of the authors, are lacking.

We have conducted multiple control experiments to exclude the possibility of contamination.

1). Western blot analysis of SLC6A17-HA immunoisolation (Figure 4D and Figure 4—figure supplement 1) has shown that this faction contained little other organelles and membranes. These results are strong argument that contaminations in our isolated fraction were in very low level.

2). We then examined the proportion of SLC6A17 localized SVs through quantifying the co-localization of Syp and SLC6A17 by anti-Syp immunoisolation in Slc6a17-2A-HA-iCre mice. We found that SLC6A17 is predominately localized on SVs (with 98.7% compared with classical SV marker, Author response image 1A). This further showed that immunoisolated SLC6A17 fraction was mainly composed of SVs.

3). We also analyzed other SV marker proteins such as Syt1 and Syb2 for IP-LC-MS, all results supported Gln enrichment (Author response image 1B).

4). Importantly, immunoisolation of the SLC6A17P633R-HA protein, which caused SLC6A17 mislocalization away from the SVs (Figure 3B and Figure 3—figure supplement 1C, D), showed no Gln enrichment (Author response image 1C).

5). Moreover, immunoisolation of AAV-PHP.eb overexpressed cytoplasmic membrane Gln transporter SLC38A1-HA did not show Gln enrichment (Author response image 1D).

6). We also tested whether trafficking organelles such as the lysosome could enrich Gln. As is shown in Author response image 1E, immunoisolation of AAV-PHP.eb overexpressed TMEM192-HA did not show Gln enrichment. For active transport, we tested the effects of proton dissipator FCCP, v-ATPase inhibitor NEM and ΔpH dissipator nigercin. As is shown in Author response image 1F, 1G, Gln level was reduced by these inhibitors, supporting active transport of Gln.

Author response image 1.

Control experiments to test for contamination. A. Anti-Syp immunoisolation in Slc6a17-2A-HA-iCre mice. B. Quantification of Gln level in anti-Syt1 and anti-Syb2 immunoisolated fraction. C. Anti-HA immunoisolation in SLC6A7-2A-HA and anti-Slc6a17P633R mice. D. Anti-HA immunoisolation in AAV-PHP.eb-hSyn-SLC38A1-HA overexperssion mice. E. Anti-HA immunoisolation in AAV-PHP.eb-hSyn-TMEM192-HA overexperssion mice. F. Anti-HA immunoisolation in SLC6A7-2A-HA mice under FCCP (50 μM) and NEM (200 μM). G. Anti-Syp immunoisolation in wild type mice under FCCP (50 μM) and Nigercin (20 μM).

B) The authors generated multiple potentially very useful genetic tools and models. However, the validation of these models is incomplete. Most importantly, it remains unclear whether the different mutations affect SLC6A17 expression levels, subcellular localization, or the expression and trafficking of other SV and synapse components.

The verification of transgenic mouse line is described in the Material and Methods section of our manuscript. There are numerous literatures published for CRISPR mediated gene editing in animals and the off-target effect of CRISPR-Cas9 system is widely studied with optimized design tools developed by many groups (Platt et al., 2014; Chu et al., 2015, 2016; Liu et al., 2017; Gemberling et al., 2021; Singh et al., 2022). The gRNAs used for animal generation were chosen carefully based on publically available tools. Apart from basic genomic PCR sequencing of target regions of all gene edited mouse models, Southern blots were performed by Biocytogen company for Slc6a17-HA-2A-iCre and Slc6a17P633R mice to rule out random insertions. Expression levels in Slc6a17-KO and Slc6a17P633R mice were not affected, as shown in Figure R2. HA-tagged protein in Slc6a17-HA-2A-iCre and Slc6a17P633R mice were detected by immunoisolation, immunofluorescence, and fractionation (Figure 3, 4, Figure 3—figure supplement 1, Figure 4—figure supplement 1). Both showed localizations expected from previous reports ().

C) Apart from the caveats mentioned above regarding Gln uptake into SVs, the data interpretation provided by the authors lacks stringency with respect to the biophysics of plasma membrane and SV transporters.

The biophysics of SLC6A17 was carefully studied (Para et al 2008; Zaia and Reimer, 2009). Our work focused on in vivo biochemical results, not biophysics.

Author response image 2.

Verification of genetic mouse models. A. q-PCR verification of Slc6a17-KO mice; B. q-PCR verification of Slc6a17P633R mice; C. Example of genomic primer design for Slc6a17-HA-2A-iCre mice founder mice screen; D. Example of genomic PCR for Slc6a17-HA-2A-iCre mice founder mice screen; E. Southern blot performed for Slc6a17-HA-2A-iCre mice.

Reference

Chu, Van Trung et al. “Increasing the efficiency of homology-directed repair for CRISPR-Cas9-induced precise gene editing in mammalian cells.” Nature biotechnology vol. 33,5 (2015): 543-8. doi:10.1038/nbt.3198

Chu, Van Trung, et al. "Efficient generation of Rosa26 knock-in mice using CRISPR/Cas9 in C57BL/6 zygotes." BMC biotechnology 16.1 (2016): 1-15.

Gemberling, Matthew P et al. “Transgenic mice for in vivo epigenome editing with CRISPR-based systems.” Nature methods vol. 18,8 (2021): 965-974. doi:10.1038/s41592-021-01207-2

Liu, Edison T., et al. "Of mice and CRISPR: The post‐CRISPR future of the mouse as a model system for the human condition." EMBO reports 18.2 (2017): 187-193.

Madisen, Linda, et al. "A robust and high-throughput Cre reporting and characterization system for the whole mouse brain." Nature neuroscience 13.1 (2010): 133-140.

Parra, Leonardo A., et al. "The orphan transporter Rxt1/NTT4 (SLC6A17) functions as a synaptic vesicle amino acid transporter selective for proline, glycine, leucine, and alanine." Molecular pharmacology 74.6 (2008): 15211532.

Platt, R.J., Chen, S., Zhou, Y., Yim, M.J., Swiech, L., Kempton, H.R., Dahlman, J.E., Parnas, O., Eisenhaure, T.M., Jovanovic, M., et al. (2014). CRISPR-Cas9 knockin mice for genome editing and cancer mode Yang, Hui, Haoyi Wang, and Rudolf Jaenisch. "Generating genetically modified mice using CRISPR/Cas-mediated genome engineering." Nature protocols 9.8 (2014): 1956-1968.ling. Cell 159, 440-455.

Singh, Surender et al. “Opportunities and challenges with CRISPR-Cas mediated homologous recombination based precise editing in plants and animals.” Plant molecular biology, 10.1007/s11103-022-01321-5. 31 Oct. 2022, doi:10.1007/s11103-022-01321-5

Zaia, K.A., and Reimer, R.J. (2009). Synaptic vesicle protein NTT4/XT1 (SLC6A17) catalyzes Na+-coupled neutral amino acid transport. J Biol Chem 284, 8439-8448.

Author Response

eLife assessment

In this valuable study, the authors investigate the mechanism of amyloid nucleation in a cellular system using their novel ratiometric measurements and uncover interesting insights regarding the role of polyglutamine length and the sequence features of glutamine-rich regions on amyloid formation. Overall, the problem is significant and being able to assess nucleation in cells is of considerable relevance. The data, as presented and analyzed, are currently still incomplete. The specific claims would be stronger if based on in vitro measurements that avoid the intricacies of specific cellular systems and that are more suitable for assessing sequence-intrinsic properties.

We are pleased that the editors find our study valuable. We find that the reviewers’ criticisms largely arise from misunderstandings inherent to the conceptually challenging nature of the topic, rather than fundamental flaws, as we will elaborate here. We are grateful for the opportunity afforded by eLife to engage reviewers in a constructive public dialogue.

Reviewer #1 (Public Review):

The authors take on the challenge of defining the core nucleus for amyloid formation by polyglutamine tracts. This rests on the assertion that polyQ forms amyloid structures to the exclusion of all other forms of solids. Using their unique assay, deployed in yeast, the authors attempt to infer the size of the nucleus that templates amyloid formation by polyQ. Further, through a series of sequence titrations, all studied using a single type of assay, the authors converge on an assertion stating that a single polyQ molecule is the nucleus for amyloid formation, that 12-residues make up the core of the nucleus, that it takes ca. 60 Qs in a row to unmask this nucleation potential, and that polyQ amyloid formation belongs to the same universality class as self-poisoned crystallization, which is the hallmark of crystallization from polymer melts formed by large, high molecular weight synthetic polymers. Unfortunately, the authors have decided to lean in hard on their assertions without a critical assessment of whether their findings stand up to scrutiny. If their findings are truly an intrinsic property of polyQ molecules, then their findings should be reconstituted in vitro. Unfortunately, careful and rigorous experiments in vitro show that there is a threshold concentration for forming fibrillar solids. This threshold concentration depends on the flanking sequence context on temperature and on solution conditions. The existence of a threshold concentration defies the expectation of a monomer nucleus. The findings disagree with in vitro data presented by Crick et al., and ignored by the authors. Please see: https://doi.org/10.1073/pnas.1320626110. These reports present data from very different assays, the importance of which was underscored first by Regina Murphy and colleagues. The work of Crick et al., provides a detailed thermodynamic framework - see the SI Appendix. This framework dove tails with theory and simulations of Zhang and Muthukumar, which explains exactly how a system like polyQ might work (https://doi.org/10.1063/1.3050295). The picture one paints is radically different from what the authors converge upon. One is inclined to lean toward data that are gleaned using multiple methods in vitro because the test tube does not have all the confounding effects of a cellular milieu, especially when it comes to focusing on sequence-intrinsic conformational transitions of a protein. In addition to concerns about the limitations of the DAmFRET method, which based on the work of the authors in their collaborative paper by Posey et al., are being stretched to the limit, there is the real possibility that the cellular milieu, unique to the system being studied, is enabling transitions that are not necessarily intrinsic to the sequence alone. A nod in this direction is the work of Marc Diamond, which showed that having stabilized the amyloid form of Tau through coacervation, there is a large barrier that limits the loss of amyloid-like structure for Tau. There may well be something similar going on with the polyQ system. If the authors could show that their data are achievable in vitro without anything but physiological buffers one would have more confidence in a model that appears to contradict basic physical principles of how homopolymers self-assemble. Absent such additional evidence, numerous statements seem to be too strong. There are also several claims that are difficult to understand or appreciate.

Rebuttal to the perceived necessity of in vitro experiments

The overarching concern of this reviewer and reviewing editor is whether in-cell assays can inform on sequence-intrinsic properties. We understand this concern. We believe however that the relative merit of in-cell assays is largely a matter of perspective. The truly sequence-intrinsic behavior of polyQ, i.e. in a vacuum, is less informative than the “sequence-intrinsic” behaviors of interest that emerge in the presence of extraneous molecules from the appropriate biological context. In vitro experiments typically include a tiny number of these -- water, ions, and sometimes a crowding agent meant to approximate everything else. Obviously missing are the myriad quinary interactions with other proteins that collectively round out the physiological solvent. The question is what experimental context best approximates that of a living human neuron under which the pathological sequence-dependent properties of polyQ manifest. We submit that a living yeast cell comes closer to that ideal than does buffer in a test tube.

The reviewer’s statements that our findings must be validated in vitro ignores the fact -- stressed in our introduction -- that decades of in vitro work have not yet generated definitive evidence for or against any specific nucleus model. In addition to the above, one major problem concerns the large sizes of in vitro systems that obscure the effects of primary nucleation. For example, a typical in vitro experimental volume of e.g. 1.5 ml is over one billion-fold larger than the femtoliter volume of a cell. This means that any nucleation-limited kinetics of relevant amyloid formation are lost, and any alternative amyloid polymorphs that have a kinetic growth advantage -- even if they nucleate at only a fraction the rate of relevant amyloid -- will tend to dominate the system (Buell, 2017). Novel approaches are clearly needed to address these problems. We present such an approach, stretch it to the limit (as the reviewer notes) across multiple complementary experiments, and arrive at a novel finding that is fully and uniquely consistent with all of our own data as well as the collective prior literature.

That the preceding considerations are collectively essential to understand relevant amyloid behavior is evident from recent cryoEM studies showing that in vitro-generated amyloid structures generally differ from those in patients (Arseni et al., 2022; Bansal et al., 2021; Radamaker et al., 2021; Schmidt et al., 2019; Schweighauser et al., 2020; Yang et al., 2022). This is highly relevant to the present discourse because each amyloid structure is thought to emanate from a different nucleating structure. This means that in vitro experiments have broadly missed the mark in terms of the relevant thermodynamic parameters that govern disease onset and progression. Note that the rules laid out via our studies are not only consistent with structural features of polyQ amyloid in cells, but also (as described in the discussion) explain why the endogenous structure of a physiologically relevant Q zipper amyloid differs from that of polyQ.

A recent collaboration between the Morimoto and Knowles groups (Sinnige et al.) investigated the kinetics of aggregation by Q40-YFP expressed in C. elegans body wall muscle cells, using quantitative approaches that have been well established for in vitro amyloid-forming systems of the type favored by the reviewer. They calculate a reaction order of just 1.6, slightly higher than what would be expected for a monomeric nucleus but nevertheless fully consistent with our own conclusions when one accounts for the following two aspects of their approach. First, the polyQ tract in their construct is flanked by short poly-Histidine tracts on both sides. These charges very likely disfavor monomeric nucleation because all possible configurations of a four-stranded bundle position the beginning and end of the Q tract in close proximity, and Q40 is only just long enough to achieve monomeric nucleation in the absence of such destabilization. Second, the protein is fused to YFP, a weak homodimer (Landgraf et al., 2012; Snapp et al., 2003). With these two considerations, our model -- which was generated from polyQ tracts lacking flanking charges or an oligomeric fusion -- predicts that amyloid nucleation by their construct will occur more frequently as a dimer than a monomer. Indeed, their observed reaction order of 1.6 supports a predominantly dimeric nucleus. Like us and others, Sinnige et al. did not observe phase separation prior to amyloid formation. This is important because it not only argues against nucleation occurring in a condensate, it also suggests that the reaction order they calculated has not been limited by the concentration-buffering effect of phase separation.

While we agree that our conclusions rest heavily on DAmFRET data (for good reason), we do provide supporting evidence from molecular dynamics simulations, SDD-AGE, and microscopy.

To summarize, given the extreme limitations of in vitro experiments in this field, the breadth of our current study, and supporting findings from another lab using rigorous quantitative approaches, we feel that our claims are justified without in vitro data.

Rebuttal to the perceived incompatibility of monomeric nucleation with the existence of a critical concentration for amyloid

We appreciate that the concept of a monomeric nucleus can superficially appear inconsistent with the fact that crystalline solids such as polyQ amyloid have a saturating concentration, but this is only true if one neglects that polyQ amyloids are polymer crystals with intramolecular ordering. The perceived discrepancy is perhaps most easily dispelled by protein crystallography. Folded proteins form crystals. These crystals have critical concentrations, and the protein subunits within them each have intramolecular crystalline order (in the form of secondary structure). To extrapolate these familiar examples to our present finding with polyQ, one need only appreciate the now well-established phenomenon of secondary nucleation, whereby transient interactions of soluble species with the ordered species leads to their own ordering (Törnquist et al., 2018). Transience is important here because it implies that intramolecular ordering can in principle propagate even in solutions that are subsaturated with respect to bulk crystallization. This is possible in the present case because the pairing of sufficiently short beta strands (equivalent to “stems” in the polymer crystal literature) will be more stable intramolecularly than intermolecularly, due to the reduced entropic penalty of the former. Our elucidation that Q zipper ordering can occur with shorter strands intramolecularly than intermolecularly (Fig. S4C-D) demonstrates this fact. It is also evident from published descriptions of single molecule “crystals” formed in sufficiently dilute solutions of sufficiently long polymers (Hong et al., 2015; Keller, 1957; Lauritzen and Hoffman, 1960).

In suggesting that a saturating concentration for amyloid rules out monomeric nucleation, the reviewer assumes that the Q zipper-containing monomer must be stable relative to the disordered ensemble. This is not inherent to our claim and in fact opposes the definition of a nucleus. The monomeric nucleating structure need not be more stable than the disordered state, and monomers may very well be disordered at equilibrium at low concentrations. To be clear, our claim requires that the Q zipper-containing monomer is both on pathway to amyloid and less stable than all subsequent species that are on pathway to amyloid. The former requirement is supported by our extensive mutational analysis. The latter requirement is supported by our atomistic simulations showing the Q zipper-containing monomer is stabilized by dimerization (see our 2021 preprint). Hence, requisite ordering in the nucleating monomer is stabilized by intermolecular interactions. We provide in Author response image 1 an illustration to clarify what we believe to be the discrepancy between our claim and the reviewer’s interpretation.

Author response image 1.

That the rate-limiting fluctuation for a crystalline phase can occur in a monomer can also be understood as a consequence of Ostwald’s rule of stages, which describes the general tendency of supersaturated solutes, including amyloid forming proteins (Chakraborty et al., 2023), to populate metastable phases en route to more stable phases (De Yoreo, 2022; Schmelzer and Abyzov, 2017). Our findings with polyQ are consistent with a general mechanism for Ostwald’s rule wherein the relative stabilities of competing polymorphs differ with the number of subunits (De Yoreo, 2022; Navrotsky, 2004). As illustrated in Fig. 6 of Navrotsky, a polymorph that is relatively stable at small particle sizes tends to give way to a polymorph that -- while initially unstable -- becomes more stable as the particles grow. The former is analogous to our early stage Q zipper composed of two short sheets with an intramolecular interface, while the latter is analogous to the later stage Q zipper composed of longer sheets with an intermolecular interface. Subunit addition stabilizes the latter more than the former, hence the initial Q zipper that is stabilized more by intra- than intermolecular interactions will mature with growth to one that is stabilized more by intermolecular interactions.

We apologize to the Pappu group for neglecting to cite Crick et al. 2013 in the current preprint. Contrary to the reviewer’s assessment, however, we find that the conclusions of this valuable study do more to support than to refute our findings. Briefly, Crick et al. investigated the aggregation of synthetic Q30 and Q40 peptides in vitro, wherein fibrils assembled from high concentrations of peptide were demonstrated to have saturating concentrations in the low micromolar range. As explained above, this finding of a saturating concentration does not refute our results. More relevant to the present work are their findings that “oligomers” accumulated over an hours-long timespan in solutions that are subsaturated with respect to fibrils, and these oligomers themselves have (nanomolar) critical concentrations. The authors postulated that the oligomers result from liquid–liquid demixing of intrinsically disordered polyglutamine. However, phase separation by a peptide is expected to fix its concentration in both the solute and condensed phases, and, because disordered phase separation is inherently faster than amyloid formation, the postulated explanation removes the driving force for any amyloid phase with a critical solubility greater than that of the oligomers. In place of this interpretation that truly does appear to -- in the reviewer’s words -- “contradict basic physical principles of how homopolymers self-assemble”, we interpret these oligomers as evidence of our Q zipper-containing self-poisoned multimers, rounded as an inherent consequence of self-poisoning (Ungar et al., 2005), and likely akin to semicrystalline spherulites that have been observed in other polymer crystal and amyloid-forming systems (Crist and Schultz, 2016; Vetri and Foderà, 2015). That Crick et al. also observed the formation of a relatively labile amyloid phase when the reactions were started with 50 uM peptide is unsurprising in light of the aforementioned kinetic advantage that large reaction volumes can confer to labile polymorphs, and that high concentrations (in this case, orders of magnitude higher than the likely physiological concentration of polyQ (Wild et al., 2015)) can favor the formation of labile amyloid polymorphs (Ohhashi et al., 2010). Indeed, a contemporaneous study by the Wetzel group using very similar peptide constructs and polyQ lengths -- but beginning with lower concentrations -- found that the relevant saturating concentrations for amyloid lie below their limit of detection of 100 nM (Sahoo et al., 2014).

Rebuttals to other critiques

The reviewer states that we found nucleation potential to require 60 Qs in a row. Our data are collectively consistent with nucleation occurring at and above approximately 36 Qs, a point repeated in the paper. The reviewer may be referring to our statement, ”Sixty residues proved to be the optimum length to observe both the pre- and post-nucleated states of polyQ in single experiments”. The purpose of this statement is simply to describe the practical consideration that led us to use 60 Qs for the bulk of our assays. We do appreciate that the fraction of AmFRET-positive cells is very low for lengths just above the threshold, especially Q40. They are nevertheless highly significant (p = 0.004 in [PIN+] cells, one-tailed T-test), and we will modify the figure and text to clarify this.

The reviewer characterizes self-poisoning as the hallmark of crystallization from polymer melts, which would be problematic for our conclusions if self-poisoning were limited to this non-physiological context. In fact the term was first used to describe crystallization from solution (Organ et al., 1989), wherein the phenomenon is more pronounced (Ungar et al., 2005).

Reviewer #2 (Public Review):

Numerous neurodegenerative diseases are thought to be driven by the aggregation of proteins into insoluble filaments known as "amyloids". Despite decades of research, the mechanism by which proteins convert from the soluble to insoluble state is poorly understood. In particular, the initial nucleation step is has proven especially elusive to both experiments and simulation. This is because the critical nucleus is thermodynamically unstable, and therefore, occurs too infrequently to directly observe. Furthermore, after nucleation much faster processes like growth and secondary nucleation dominate the kinetics, which makes it difficult to isolate the effects of the initial nucleation event. In this work Kandola et al. attempt to surmount these obstacles using individual yeast cells as microscopic reaction vessels. The large number of cells, and their small size, provides the statistics to separate the cells into pre- and post-nucleation populations, allowing them to obtain nucleation rates under physiological conditions. By systematically introducing mutations into the amyloid-forming polyglutamine core of huntingtin protein, they deduce the probable structure of the amyloid nucleus. This work shows that, despite the complexity of the cellular environment, the seemingly random effects of mutations can be understood with a relatively simple physical model. Furthermore, their model shows how amyloid nucleation and growth differ in significant ways, which provides testable hypotheses for probing how different steps in the aggregation pathway may lead to neurotoxicity.

In this study Kandola et al. probe the nucleation barrier by observing a bimodal distribution of cells that contain aggregates; the cells containing aggregates have had a stochastic fluctuation allowing the proteins to surmount the barrier, while those without aggregates have yet to have a fluctuation of suitable size. The authors confirm this interpretation with the selective manipulation of the PIN gene, which provides an amyloid template that allows the system to skip the nucleation event.

In simple systems lacking internal degrees of freedom (i.e., colloids or rigid molecules) the nucleation barrier comes from a significant entropic cost that comes from bringing molecules together. In large aggregates this entropic cost is balanced by attractive interactions between the particles, but small clusters are unable to form the extensive network of stabilizing contacts present in the larger aggregates. Therefore, the initial steps in nucleation incur an entropic cost without compensating attractive interactions (this imbalance can be described as a surface tension). When internal degrees of freedom are present, such as the conformational states of a polypeptide chain, there is an additional contribution to the barrier coming from the loss of conformational entropy required to the adopt aggregation-prone state(s). In such systems the clustering and conformational processes do not necessarily coincide, and a major challenge studying nucleation is to separate out these two contributions to the free energy barrier. Surprisingly, Kandola et al. find that the critical nucleus occurs within a single molecule. This means that the largest contribution to the barrier comes from the conformational entropy cost of adopting the beta-sheet state. Once this state is attained, additional molecules can be recruited with a much lower free energy barrier.

There are several caveats that come with this result. First, the height of the nucleation barrier(s) comes from the relative strength of the entropic costs compared to the binding affinities. This balance determines how large a nascent nucleus must grow before it can form interactions comparable to a mature aggregate. In amyloid nuclei the first three beta strands form immature contacts consisting of either side chain or backbone contacts, whereas the fourth strand is the first that is able to form both kinds of contacts (as in a mature fibril). This study used relatively long polypeptides of 60 amino acids. This is greater than the 20-40 amino acids found in amyloid-forming molecules like ABeta or IAPP. As a result, Kandola et al.'s molecules are able to fold enough times to create four beta strands and generate mature contacts intramolecularly. The authors make the plausible claim that these intramolecular folds explain the well-known length threshold (L~35) observed in polyQ diseases. The intramolecular folds reduce the importance of clustering multiple molecules together and increase the importance of the conformational states. Similarly, manipulating the sequence or molecular concentrations will be expected to manipulate the relative magnitude of the binding affinities and the clustering entropy, which will shift the relative heights of the entropic barriers.

The reviewer correctly notes that the majority of our manipulations were conducted with 60-residue long tracts (which corresponds to disease onset in early adulthood), and this length facilitates intramolecular nucleation. However, we also analyzed a length series of polyQ spanning the pathological threshold, as well as a synthetic sequence designed explicitly to test the model nucleus structure with a tract shorter than the pathological threshold, and both experiments corroborate our findings.

The authors make an important point that the structure of the nucleus does not necessarily resemble that of the mature fibril. They find that the critical nucleus has a serpentine structure that is required by the need to form four beta strands to get the first mature contacts. However, this structure comes at a cost because residues in the hairpins cannot form strong backbone or zipper interactions. Mature fibrils offer a beta sheet template that allows incoming molecules to form mature contacts immediately. Thus, it is expected that the role of the serpentine nucleus is to template a more extended beta sheet structure that is found in mature fibrils.

A second caveat of this work is the striking homogeneity of the nucleus structure they describe. This homogeneity is likely to be somewhat illusory. Homopolymers, like polyglutamine, have a discrete translational symmetry, which implies that the hairpins needed to form multiple beta sheets can occur at many places along the sequence. The asparagine residues introduced by the authors place limitations on where the hairpins can occur, and should be expected to increase structural homogeneity. Furthermore, the authors demonstrate that polyglutamine chains close to the minimum length of ~35 will have strict limitations on where the folds must occur in order to attain the required four beta strands.

We are unsure how to interpret the above statements as a caveat. We agree that increasing sequence complexity will tend to increase homogeneity, but this is exactly the motivation of our approach. We explicitly set out to determine the minimal complexity sequence sufficient to specify the nucleating conformation, which we ultimately identified in terms of secondary and tertiary structure. We do not specify which parts of a long polyQ tract correspond to which parts of the structure, because, as the reviewer points out, they can occur at many places. Hence, depending on the length of the polyQ tract, the nucleus we describe may have any length of sequence connecting the strand elements. We do not think that the effects of N-residue placement can be interpreted as a confounding influence on hairpin position because the striking even-odd pattern we observe implicates the sides of beta strands rather than the lengths. Moreover, we observe this pattern regardless of the residue used (Gly, Ser, Ala, and His in addition to Asn).

A novel result of this work is the observation of multiple concentration regimes in the nucleation rate. Specifically, they report a plateau-like regime at intermediate regimes in which the nucleation rate is insensitive to protein concentration. The authors attribute this effect to the "self-poisoning" phenomenon observed in growth of some crystals. This is a valid comparison because the homogeneity observed in NMR and crystallography structures of mature fibrils resemble a one-dimensional crystal. Furthermore, the typical elongation rate of amyloid fibrils (on the order of one molecule per second) is many orders of magnitude slower than the molecular collision rate (by factors of 10^6 or more), implying that the search for the beta-sheet state is very slow. This slow conformational search implies the presence of deep kinetic traps that would be prone to poisoning phenomena. However, the observation of poisoning in nucleation during nucleation is striking, particularly in consideration of the expected disorder and concentration sensitivity of the nucleus. Kandola et al.'s structural model of an ordered, intramolecular nucleus explains why the internal states responsible for poisoning are relevant in nucleation.

We thank the reviewer for noting the novelty and plausibility of the self-poisoning connection. We would like to elaborate on our finding that self-poisoning inhibits nucleation (in addition to elongation), as this could prove confusing to some readers. While self-poisoning is claimed to inhibit primary nucleation in the polymer crystal literature (Ungar et al., 2005; Zhang et al., 2018), the semantics of “nucleation” in this context warrants clarification. Technically, the same structure can be considered a nucleus in one context but not in another. The Q zipper monomer, even if it is rate-limiting for amyloid formation at low concentrations (and is therefore the “nucleus”), is not necessarily rate-limiting when self-poisoned at high concentrations. Whether it comprises the nucleus in this case depends on the rates of Q zipper formation relative to subunit addition to the poisoned state. If the latter happens slower than Q zipper formation de novo, it can be said that self-poisoning inhibits nucleation, regardless of whether the Q zipper formed. We suspect this to be the mechanism by which preemptive oligomerization blocks nucleation in the case of polyQ, though other mechanisms may be possible.

To achieve these results the authors used a novel approach involving a systematic series of simple sequences. This is significant because, while individual experiments showed seemingly random behavior, the randomness resolved into clear trends with the systematic approach. These trends provided clues to build a model and guide further experiments.

Reviewer #3 (Public Review):

Kandola et al. explore the important and difficult question regarding the initiating event that triggers (nucleates) amyloid fibril growth in glutamine-rich domains. The researchers use a fluorescence technique that they developed, dAMFRET, in a yeast system where they can manipulate the expression level over several orders of magnitude, and they can control the length of the polyglutamine domain as well as the insertion of interfering non-glutamine residues. Using flow cytometry, they can interrogate each of these yeast 'reactors' to test for self-assembly, as detected by FRET.

In the introduction, the authors provide a fairly thorough yet succinct review of the relevant literature into the mechanisms of polyglutamine-mediated aggregation over the last two decades. The presentation as well as the illustrations in Figure 1A and 1B are difficult to understand, and unfortunately, there is no clear description of the experimental technique that would allow the reader to connect the hypothetical illustrations to the measurement outcomes. The authors do not explain what the FRET signal specifically indicates or what its intensity is correlated to. FRET measures distance between donor and acceptor, but can it be reliably taken as an indicator of a specific beta-sheet conformation and of amyloid? Does the signal increase with both nucleation and with elongation, and is the signal intensity the same if, e.g., there were 5 aggregates of 10 monomers each versus 50 monomeric nuclei? Is there a reason why the AmFRET signal intensity decreases at longer Q even though the number of cells with positive signal increases? Does the number of positive cells increase with time? The authors state later that 'non-amyloid containing cells lacked AmFRET altogether', but this seems to be a tautology - isn't the lack of AmFRET taken as a proof of lack of amyloid? Overall, a clearer description of the experimental method and what is actually measured (and validation of the quantitative interpretation of the FRET signal) would greatly assist the reader in understanding and interpreting the data.

We believe the difficulty in understanding the illustrations in Figure 1A and 1B is inherent to the subject. We agree that elaborating how DAmFRET works would help the reader, and will add a few sentences to this end. Beyond this, we refer the reviewer and readers to our cited prior work describing the theory and interpretation of DAmFRET. Note that the y-axes of DAmFRET plots are not raw FRET but rather “AmFRET”, a ratio of FRET to total expression level. As explained thoroughly in our cited prior work, the discontinuity of AmFRET with expression level indicates that the high AmFRET-population formed via a disorder-to-order transition. When the query protein is predicted to be intrinsically disordered, the discontinuous transition to high AmFRET invariably (among hundreds of proteins tested in prior published and unpublished work) signifies amyloid formation as corroborated by SDD-AGE and tinctorial assays.

When performed using standard flow cytometry as in the present study, every AmFRET measurement corresponds to a cell-wide average, and hence does not directly inform on the distribution of the protein between different stoichiometric species. As there is only one fluorophore per protein molecule, monomeric nuclei have no signal. DAmFRET can distinguish cells expressing monomers from stable dimers from higher order oligomers (see e.g. Venkatesan et al. 2019), and we are therefore quite confident that AmFRET values of zero correspond to cells in which a vast majority of the respective protein is not in homo-oligomeric species (i.e. is monomeric or in hetero-complexes with endogenous proteins). The exact value of AmFRET, even for species with the same stoichiometry, will depend both on the effect of their respective geometries on the proximity of mEos3.1 fluorophores, and on the fraction of protein molecules in the species. Hence, we only attempt to interpret the plateau values of AmFRET (where the fraction of protein in an assembled state approaches unity) as directly informing on structure, as we did in Fig. S3A.

We believe that AmFRET decreases with longer polyQ because the mass fraction of fluorophore decreases in the aggregate, simply because the extra polypeptide takes up volume in the aggregate.

Yes, the fraction of positive cells in a discontinuous DAmFRET plot does increase with time. However, given the more laborious data collection and derivation of nucleation kinetics in a system with ongoing translation, especially across hundreds of experiments with other variables, ours is a snapshot measurement to approximately derive the relative contributions of intra- and intermolecular fluctuations to the nucleation barrier, rather than the barrier’s magnitude.

We will revise the tautological statement by removing “non-amyloid containing”.

The authors demonstrate that their assay shows that the fraction of cells with AmFRET signal increases strongly with an increase in polyQ length, with a 'threshold around 50-60 glutamines. This roughly correlates with the Q-length dependence of disease. The experiments in which asparagine or other amino acids are inserted at variable positions in the glutamine repeat are creative and thorough, and the data along with the simulations provide compelling support for the proposed Q zipper model. The experiments shown in Figure 5 are strongly supportive of a model where formation of the beta-sheet nucleus is within a monomer. This is a potentially important result, as there are conflicting data in the literature as to whether the nucleus in polyQ is monomer.

We thank the reviewer for these comments. We wish to clarify one important point, however, concerning the correlation of our data with the pathological length threshold. As we state in the first results section, “Our data recapitulated the pathologic threshold -- Q lengths 35 and shorter lacked AmFRET, indicating a failure to aggregate or even appreciably oligomerize, while Q lengths 40 and longer did acquire AmFRET in a length and concentration-dependent manner”. Hence, most of our experiments were conducted with 60Q not because it resembles the pathological threshold, but rather because it was most convenient for DAmFRET experiments.

I did not find the argument, that their data shows the Q zipper grows in two dimensions, compelling; there are more direct experimental methods to answer this question. I was also confused by the section that Q zippers poison themselves. It would be easier for the reader to follow if the authors first presented their results without interpretation. The data seem more consistent with an argument that, at high concentrations, non-structured polyQ oligomers form which interfere with elongation into structured amyloid assemblies - but such oligomers would not be zippers.

Self-poisoning is a widely observed and heavily studied phenomenon in polymer crystal physics, though it seems not yet to have entered the lexicon of amyloid biologists. We were new to this concept before it emerged as an extremely parsimonious explanation for our results. As described in the text, two pieces of evidence exclude the alternative mechanism suggested by the reviewer -- that non-structured oligomers form and subsequently engage and inhibit the template. Specifically, 1) inhibition occurs without any detectable FRET, even at high total protein concentration, indicating the species do not form in a concentration-dependent manner that would be expected of disordered oligomers; and 2) inhibition itself has strict sequence requirements that match those of Q zippers. Hence our data collectively suggest that inhibition is a consequence of the deposition of partially ordered molecules onto the templating surface.

Although some speculation or hypothesizing is perfectly appropriate in the discussion, overall the authors stretch this beyond what can be supported by the results. A couple of examples: The conclusion that toxicity arises from 'self-poisoned polymer crystals' is not warranted, as there is no relevant data presented in this manuscript. The authors refer to findings 'that kinetically arrested aggregates emerge from the same nucleating event responsible for amyloid formation', but I cannot recall any evidence for this statement in the results section.

We restricted any mention of toxicity to the introduction and a section in the discussion that is not worded as conclusive. Nevertheless, we will soften the subheading and text of the relevant section in the discussion to more clearly indicate the speculative nature of the statements.

We stand by our statement 'that kinetically arrested aggregates emerge from the same nucleating event responsible for amyloid formation', as this follows directly from self-poisoning.

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Author Response

Response to Reviewer 1:

Summary of what the author was trying to achieve: In this study, the author aimed to develop a method for estimating neuronal-type connectivity from transcriptomic gene expression data, specifically from mouse retinal neurons. They sought to develop an interpretable model that could be used to characterize the underlying genetic mechanisms of circuit assembly and connectivity.

Strengths: The proposed bilinear model draws inspiration from commonly implemented recommendation systems in the field of machine learning. The author presents the model clearly and addresses critical statistical limitations that may weaken the validity of the model such as multicollinearity and outliers. The author presents two formulations of the model for separate scenarios in which varying levels of data resolution are available. The author effectively references key work in the field when establishing assumptions that affect the underlying model and subsequent results. For example, correspondence between gene expression cell types and connectivity cell types from different references are clearly outlined in Tables 1-3. The model training and validation are sufficient and yield a relatively high correlation with the ground truth connectivity matrix. Seemingly valid biological assumptions are made throughout, however, some assumptions may reduce resolution (such as averaging over cell types), thus missing potentially important single-cell gene expression interactions.

Thank you for acknowledging the strengths of this work. The assumption to average gene expression data across individual cells within a given cell type was made in response to the inherent limitations of, for example, the mouse retina dataset, where individual cell-level connectivity and gene expression data are not profiled jointly (the second scenario in our paper). This approach was a necessary compromise to facilitate the analysis at the cell type level. However, in datasets where individual cell-level connectivity and gene expression data are matched, such as the C.elegans dataset referenced below, our model can be applied to achieve single-cell resolution (the first scenario in our paper), offering a more detailed understanding of genetic underpinnings in neuronal connectivity.

Weaknesses: The main results of the study could benefit from replication in another dataset beyond mouse retinal neurons, to validate the proposed method. Dimensionality reduction significantly reduces the resolution of the model and the PCA methodology employed is largely non-deterministic. This may reduce the resolution and reproducibility of the model. It may be worth exploring how the PCA methodology of the model may affect results when replicating. Figure 5, ’Gene signatures associated with the two latent dimensions’, lacks some readability and related results could be outlined more clearly in the results section. There should be more discussion on weaknesses of the results e.g. quantification of what connectivity motifs were not captured and what gene signatures might have been missed.

I value the suggestion of validating the propose method in another dataset. In response, I found the C.elegans dataset in the references the reviewer suggested below a good candidate for this purpose, and I plan to explore this dataset and incorporate findings in the revised manuscript. I understand the concerns regarding the PCA methodology and its potential impact on the model’s resolution and reproducibility. In response, alternative methods, such as regularization techniques, will be explored to address these issues. Additionally, I agree that enhancing the clarity and readability of Figure 5, as well as including a more comprehensive discussion of the model’s limitations, would significantly strengthen the manuscript.

The main weakness is the lack of comparison against other similar methods, e.g. methods presented in Barabási, Dániel L., and Albert-László Barabási. "A genetic model of the connectome." Neuron 105.3 (2020): 435-445. Kovács, István A., Dániel L. Barabási, and Albert-László Barabási. "Uncovering the genetic blueprint of the C. elegans nervous system." Proceedings of the National Academy of Sciences 117.52 (2020): 33570-33577. Taylor, Seth R., et al. "Molecular topography of an entire nervous system." Cell 184.16 (2021): 4329-4347.

Thank you for highlighting the importance of comparing our model with others, particularly those mentioned in your comments. After reviewing these papers, I find that our bilinear model aligns closely with the methods described, especially in [1, 2]. To see this, let’s start with Equation 1 in Kovács et al. [2]:

In this equation, B represents the connectivity matrix, while X denotes the gene expression patterns of individual neurons in C.elegans. The operator O is the genetic rule operator governing synapse formation, linking connectivity with individual neuronal expression patterns. It’s noteworthy that the work of Barabási and Barabási [1] explores a specific application of this framework, focusing on O for B that represents biclique motifs in the C.elegans neural network.

To identify the the operator O, the authors sought to minimize the squared residual error:

with regularization on O.

Adopting the notation from our bilinear model paper and using Z to represent the connectivity matrix, the above becomes

Coming back to the bilinear model formulation, the optimization problem, as formulated for the C.elegans dataset where individual neuron connectivity and gene expression are accessible, takes the form:

where we consider each neuron as a distinct neuronal type. In addition, we extend the dimensions of X and Y to encompass the entire set of neurons in C.elegans, with X = Y ∈ Rn×p, where n signifies the total number of neurons and p the number of genes. Accordingly, our optimization challenge evolves into:

Upon comparison with the earlier stated equation, it becomes clear that our approach aligns consistently with the notion of O = ABT. This effectively results in a decomposition of the genetic rule operator O. This decomposition extends beyond mere mathematical convenience, offering several substantial benefits reminiscent of those seen in the collaborative filtering of recommendation systems:

• Computational Efficiency: The primary advantage of this approach is its improvement in computational efficiency. For instance, solving for O ∈ Rp×p necessitates determining p2 entries. In contrast, solving for A ∈ Rp×d and B ∈ Rp×d involves determining only 2pd entries, where p is the number of genes, and d is the number of latent dimensions. Assuming the existence of a lower-dimensional latent space (d << p) that captures the essential variability in connectivity, resolving A and B becomes markedly more efficient than resolving O. Additionally, from a computational system design perspective, inferring the connectivity of a neuron allows for caching the latent embeddings of presynaptic neurons XA or postsynaptic neurons XB with a space complexity of O(nd). This is significantly more space-efficient than caching XO or OXT, which has a space complexity of O(np). This difference is particularly notable when dealing with large numbers of neurons, such as those in the entire mouse brain. The bilinear modeling approach thus enables effective handling of large datasets, simplifying the optimization problem and reducing computational load, thereby making the model more scalable and faster to execute.

• Interpretability: The separation into A for presynaptic features and B for postsynaptic features provides a clearer understanding of the distinct roles of pre- and post- synaptic neurons in forming the connection. By projecting the pre- and post- synaptic neurons into a shared latent space through XA and YB, one can identify meaningful representations within each axis, as exemplified in different motifs from the mouse retina dataset. The linear characteristics of A and B facilitate direct evaluation of each gene’s contribution to a latent dimension. This interpretability, offering insights into the genetic factors influencing synaptic connections, is beyond what O could provide itself.

• Flexibility and Adaptability: The bilinear model’s adaptability is another strength. Much like collaborative filtering, which can manage very different user and item features, our bilinear model can be tailored to synaptic partners with genetic data from varied sources. A potential application of this model is in deciphering the genetic correlates of long-range projectomic rules, where pre- and post-synaptic neurons are processed and sequenced separately, or even involving post-synaptic targets being brain regions with genetic information acquired through bulk sequencing. This level of flexibility also allows for model adjustments or extensions to incorporate other biological factors, such as proteomics, thereby broadening its utility across various research inquiries into the determinants of neuronal connectivity.

In the study by Taylor et al. [3], the authors introduced a generalization of differential gene expressions (DGE) analysis called network DGE (nDGE) to identify genetic determinants of synaptic connections. It focuses on genes co-expressed across pairs of neurons connected, compared with pairs without connection.

As the authors acknowledged in the method part of the paper, nDGE can only examine single genes co-expressed at synaptic terminals: "While the nDGE technique introduced here is a generalization of standard DGE, interrogating the contribution of pairs of genes in the formation and maintenance of synapses between pairs of neurons, nDGE can only account for a single co-expressed gene in either of the two synaptic terminals (pre/post)."

In contrast, the bilinear model offers a more comprehensive analysis by seeking a linear combination of gene expressions in both pre- and post-synaptic neurons. This model goes beyond the scope of examining individual co-expressed genes, as it incorporates different weights for the gene expressions of pre- and post-synaptic neurons. This feature of the bilinear model enables it to capture not only homogeneous but also complex and heterogeneous genetic interactions that are pivotal in synaptic connectivity. This highlights the bilinear model’s capability to delve into the intricate interactions of synaptic gene expression.

Appraisal of whether the author achieved their aims, and whether results support their conclusions: The author achieved their aims by recapitulating key connectivity motifs from single-cell gene expression data in the mouse retina. Furthermore, the model setup allowed for insight into gene signatures and interactions, however could have benefited from a deeper evaluation of the accuracy of these signatures. The author claims the method sets a new benchmark for single-cell transcriptomic analysis of synaptic connections. This should be more rigorously proven. (I’m not sure I can speak on the novelty of the method)

I value your appraisal. In response, additional validation of the bilinear model on a second dataset will be undertaken.

Discussion of the likely impact of the work on the field, and the utility of methods and data to the community : This study provides an understandable bilinear model for decoding the genetic programming of neuronal type connectivity. The proposed model leaves the door open for further testing and comparison with alternative linear and/or non-linear models, such as neural networkbased models. In addition to more complex models, this model can be built on to include higher resolution data such as more gene expression dimensions, different types of connectivity measures, and additional omics data.

Thank you for your positive assessment of the potential impact of the study.

Response to Reviewer 2:

Summary: In this study, Mu Qiao employs a bilinear modeling approach, commonly utilized in recommendation systems, to explore the intricate neural connections between different pre- and post-synaptic neuronal types. This approach involves projecting single-cell transcriptomic datasets of pre- and post-synaptic neuronal types into a latent space through transformation matrices. Subsequently, the cross-correlation between these projected latent spaces is employed to estimate neuronal connectivity. To facilitate the model training, connectomic data is used to estimate the ground-truth connectivity map. This work introduces a promising model for the exploration of neuronal connectivity and its associated molecular determinants. However, it is important to note that the current model has only been tested with Bipolar Cell and Retinal Ganglion Cell data, and its applicability in more general neuronal connectivity scenarios remains to be demonstrated.

Strengths: This study introduces a succinct yet promising computational model for investigating connections between neuronal types. The model, while straightforward, effectively integrates singlecell transcriptomic and connectomic data to produce a reasonably accurate connectivity map, particularly within the context of retinal connectivity. Furthermore, it successfully recapitulates connectivity patterns and helps uncover the genetic factors that underlie these connections.

Thank you for your positive assessment of the paper.

Weaknesses:

1. The study lacks experimental validation of the model’s prediction results.

Thank you for pointing out the importance of experimental validation. I acknowledge that the current version of the study is focused on the development and validation of the computational model, using the datasets presently available to us. Moving forward, I plan to collaborate with experimental neurobiologists. These collaborations are aimed at validating our model’s predictions, including the delta-protocadherins mentioned in the paper. However, considering the extensive time and resources required for conducting and interpreting experimental results, I believe it is more pragmatic to present a comprehensive experimental study, including the design and execution of experiments informed by the model’s predictions, in a separate follow-up paper. I intend to include a paragraph in the discussion of this paper outlining the future direction for experimental validation.

1. The model’s applicability in other neuronal connectivity settings has not been thoroughly explored.

I recognize the importance of assessing the model across different neuronal systems. In response to similar feedback from Reviewer 1, I am keen to extend the study to include the C.elegans dataset mentioned earlier. The results from applying our bilinear model to the second dataset will be incorporated into the revised manuscript.

1. The proposed method relies on the availability of neuronal connectomic data for model training, which may be limited or absent in certain brain connectivity settings.

The concern regarding the dependency of our model on the availability of connectomic data is valid. While complete connectomes are available for organisms like C.elegans and Drosophila, and efforts are underway to map the connectome of the entire mouse brain, such data may not always be accessible for all research contexts. Recognizing this limitation, part of the ongoing research is to explore ways to adapt our model to the available data, such as projectomic data. Furthermore, our bilinear model is compatible with trans-synaptic virus-based sequencing techniques [4, 5], allowing us to leverage data from these experimental approaches to uncover the genetic underpinnings of neuronal connectivity. These initiatives are crucial steps towards broadening the applicability of our model, ensuring its relevance and usefulness in diverse brain connectivity studies where detailed connectomic data may not be readily available.

References

[1] Dániel L. Barabási and Albert-László Barabási. A genetic model of the connectome. Neuron, 105(3):435–445, 2020.

[2] István A. Kovács, Dániel L. Barabási, and Albert-László Barabási. Uncovering the genetic blueprint of the c. elegans nervous system. Proceedings of the National Academy of Sciences, 117(52):33570–33577, 2020.

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Author Response

Reviewer 1 (Public Review):

1. With respect to the predictions, the authors propose that the subjects, depending on their linguistic background and the length of the tone in a trial, can put forward one or two predictions. The first is a short-term prediction based on the statistics of the previous stimuli and identical for both groups (i.e. short tones are expected after long tones and vice versa). The second is a long-term prediction based on their linguistic background. According to the authors, after a short tone, Basque speakers will predict the beginning of a new phrasal chunk, and Spanish speakers will predict it after a long tone.

In this way, when a short tone is omitted, Basque speakers would experience the violation of only one prediction (i.e. the short-term prediction), but Spanish speakers will experience the violation of two predictions (i.e. the short-term and long-term predictions), resulting in a higher amplitude MMN. The opposite would occur when a long tone is omitted. So, to recap, the authors propose that subjects will predict the alternation of tone durations (short-term predictions) and the beginning of new phrasal chunks (long-term predictions).

The problem with this is that subjects are also likely to predict the completion of the current phrasal chunk. In speech, phrases are seldom left incomplete. In Spanish is very unlikely to hear a function-word that is not followed by a content-word (and the opposite happens in Basque). On the contrary, after the completion of a phrasal chunk, a speaker might stop talking and a silence might follow, instead of the beginning of a new phrasal chunk.

Considering that the completion of a phrasal chunk is more likely than the beginning of a new one, the prior endowed to the participants by their linguistic background should make us expect a pattern of results actually opposite to the one reported here.

Response: We acknowledge the plausibility of the hypothesis advanced by Reviewer #1. We would like to further clarify the rationale that led us to predict that the hypothesized long-term predictions should manifest at the onset of (and not within) a “phrasal chunk”. The hypothesis does not directly concern the probability of a short event to follow a long one (or the other way around), which to our knowledge has not been systematically quantified in previous cross-linguistic studies. Rather, it concerns how the auditory system forms higher-level auditory chunks based on the rhythmic properties of the native language, which is what the previous behavioral studies on perceptual grouping have addressed (e.g., Iversen 2008; Molnar et al. 2014; Molnar et al. 2016). When presented with sequences of two tones alternating in duration, Spanish speakers typically report perceiving the auditory stream as a repetition of short-long chunks separated by a pause, while speakers of Basque usually report the opposite long-short grouping bias. These results suggest that the auditory system performs a chunking operation by grouping pairs of tones into compressed, higher-level auditory units (often perceived as a single event). The way two constituent tones are combined depends on linguistic experience. Based on this background, we hypothesized the presence of (i) a short-term system that merely encodes a repetition of alternations rule and predicts transitions from one constituent tone to the other (a → b → a → b, etc.); (ii) a long-term system that encodes a repetition of concatenated alternations rule and predicts transitions from one high-level unit to the other (ab → ab, etc.). Under this view, we expect predictions based on the long-term system to be stronger at the onset of (rather than within) high-level units and therefore omissions of the first constituent tone to elicit larger responses than omissions of the second constituent tone.

In other words, the omission of the onset tone would reflect the omission of the whole chunk. On the other hand, the omission of the internal tone would be better handled by the short-term system, involved in processing the low-level structure of our sequences.

A similar concern was also raised by Reviewer #2. We will include the view proposed by Reviewer #1 and Reviewer #2 in the updated version of the manuscript.

1. The authors report an interaction effect that modulates the amplitude of the omission response, but caveats make the interpretation of this effect somewhat uncertain. The authors report a widespread omission response, which resembles the classical mismatch response (in MEG) with strong activations in sensors over temporal regions. Instead, the interaction found is circumscribed to four sensors that do not overlap with the peaks of activation of the omission response.

Response: We appreciate that all three reviewers agreed on the robustness of the data analysis pipeline. The approach employed to identify the presence of an interaction effect was indeed conservative, using a non-parametric test on combined gradiometers data, no a priori assumptions regarding the location of the effect, and small cluster thresholds (cfg.clusteralpha = 0.05) to enhance the likelihood of detecting highly localized clusters with large effect sizes. This approach led to the identification of the cluster illustrated in Figure 2c, where the interaction effect is evident. The fact that this interaction effect arises in a relatively small cluster of sensors does not alter its statistical robustness. The only partial overlap of the cluster with the activation peaks might simply reflect the fact that distinct sources contribute to the generation of the omission-MMN, which has been demonstrated in numerous prior studies (e.g., Zhang et al., 2018; Ross & Hamm, 2020).

Furthermore, the boxplot in Figure 2E suggests that part of the interaction effect might be due to the presence of two outliers (if removed, the effect is no longer significant). Overall, it is possible that the reported interaction is driven by a main effect of omission type which the authors report, and find consistently only in the Basque group (showing a higher amplitude omission response for long tones than for short tones). Because of these points, it is difficult to interpret this interaction as a modulation of the omission response.

Response: The two participants mentioned by Reviewer #1, despite being somewhat distant from the rest of the group, are not outliers according to the standard Tukey’s rule. As shown in Author response image 1 below, no participant fell outside the upper (Q3+1.5xIQR) and lower whiskers (Q1-1.5xIQR) of the boxplot.

Author response image 1.

The presence of a main effect of omission type does not impact the interpretation of the interaction, especially considering that these effects emerge over distinct clusters of channels.

The code to generate Author response image 1 and the corresponding statistics have been added to the script “analysis_interaction_data.R” in the OSF folder (https://osf.io/6jep8/).

It should also be noted that in the source analysis, the interaction only showed a trend in the left auditory cortex, but in its current version the manuscript does not report the statistics of such a trend.

Response: Our interpretation of the results for the present study is mainly driven by the effect observed on sensor-level data, which is statistically robust. The source modeling analyses (in non-invasive electrophysiology) provide a possible model of the candidate brain sources driving the effect observed at the sensor level. The source showing the interactive effect in our study is the left auditory cortex. More details and statistics will be provided in the reviewed version of the manuscript.

Reviewer #2 (Public Review):

1. Despite the evidence provided on neural responses, the main conclusion of the study reflects a known behavioral effect on rhythmic sequence perceptual organization driven by linguistic background (Molnar et al. 2016, particularly). Also, the authors themselves provide a good review of the literature that evidences the influence of long-term priors in neural responses related to predictive activity. Thus, in my opinion, the strength of the statements the authors make on the novelty of the findings may be a bit far-fetched in some instances.

Response: We will consider the suggestion of reviewer #2 for the new version of the manuscript. Overall, we believe that the novelty of the current study lies in bridging together findings from two research fields - basic auditory neuroscience and cross-linguistic research - to provide evidence for a predictive coding model in the auditory that uses long-term priors to make perceptual inferences.

1. Albeit the paradigm is well designed, I fail to see the grounding of the hypotheses laid by the authors as framed under the predictive coding perspective. The study assumes that responses to an omission at the beginning of a perceptual rhythmic pattern will be stronger than at the end. I feel this is unjustified. If anything, omission responses should be larger when the gap occurs at the end of the pattern, as that would be where stronger expectations are placed: if in my language a short sound occurs after a long one, and I perceptually group tone sequences of alternating tone duration accordingly, when I hear a short sound I will expect a long one following; but after a long one, I don't necessarily need to expect a short one, as something else might occur.

Response: A similar point was advanced by Reviewer #1. We tried to clarify our hypothesis (see above). We will consider including this interpretation in the updated version of the manuscript.

1. In this regard, it is my opinion that what is reflected in the data may be better accounted for (or at least, additionally) by a different neural response to an omission depending on the phase of an underlying attentional rhythm (in terms of Large and Jones rhythmic attention theory, for instance) and putative underlying entrained oscillatory neural activity (in terms of Lakatos' studies, for instance). Certainly, the fact that the aligned phase may differ depending on linguistic background is very interesting and would reflect the known behavioral effect.

Response: We thank the reviewer for this comment, which is indeed very pertinent. Below are some comments highlighting our thoughts on this.

1) We will explore in more detail the possibility that the aligned phase may differ depending on linguistic background, which is indeed very interesting. However, we believe that even if a phase modulation by language experience is found, it would not negate the possibility that the group differences in the MMN are driven by different long-term predictions. Rather, since the hypothesized phase differences would be driven by long-term linguistic experience, phase entrainment may reflect a mechanism through which long-term predictions are carried. On this point, we agree with the Reviewer when says that “this view would not change the impact of the results but add depth to their interpretation”.

2) Related to the point above: Despite evoked responses and oscillations are often considered distinct electrophysiological phenomena, current evidence suggests that these phenomena are interconnected (e.g., Studenova et al., 2023). In our view, the hypotheses that the MMN reflects differences in phase alignment and long-term prediction errors are not mutually exclusive.

3) Despite the plausibility of the view proposed by reviewer #2, many studies in the auditory neuroscience literature putatively consider the MMN as an index of prediction error (e.g., Bendixen et al., 2012; Heilbron and Chait, 2018). There are good reasons to believe that also in our study the MMN reflects, at least in part, an error response.

In the updated version of the manuscript, we will include a paragraph discussing the possibility that the reported group differences in the omission MMN might be partially accounted for by differences in neural entrainment to the rhythmic sound sequences.

Reviewer #3 (Public Review):

The main weaknesses are the strength of the effects and generalisability. The sample size is also relatively small by today's standards, with N=20 in each group. Furthermore, the crucial effects are all mostly in the .01>P<.05 range, such as the crucial interaction P=.03. It would be nice to see it replicated in the future, with more participants and other languages. It would also have been nice to see behavioural data that could be correlated with neural data to better understand the real-world consequences of the effect.

Response: We appreciate the positive feedback from Reviewer #3. Concerning this weakness highlighted: we agree with Reviewer #3 that it would be nice to see this study replicated in the future with larger sample sizes and a behavioral counterpart. Overall, we hope this work will lead to more studies using cross-linguistic/cultural comparisons to assess the effect of experience on neural processing. In the context of the present study, we believe that the lack of behavioral data does not undermine the main findings of this study, given the careful selection of the participants and the well-known robustness of the perceptual grouping effect (e.g., Iversen 2008; Yoshida et al., 2010; Molnar et al. 2014; Molnar et al. 2016). As highlighted by Reviewer #2, having Spanish and Basque dominant “speakers as a sample equates that in Molnar et al. (2016), and thus overcomes the lack of direct behavioral evidence for a difference in rhythmic grouping across linguistic groups. Molnar et al. (2016)'s evidence on the behavioral effect is compelling, and the evidence on neural signatures provided by the present study aligns with it.”

References

1. Bendixen, A., SanMiguel, I., & Schröger, E. (2012). Early electrophysiological indicators for predictive processing in audition: a review. International Journal of Psychophysiology, 83(2), 120-131.

2. Heilbron, M., & Chait, M. (2018). Great expectations: is there evidence for predictive coding in auditory cortex?. Neuroscience, 389, 54-73.

3. Iversen, J. R., Patel, A. D., & Ohgushi, K. (2008). Perception of rhythmic grouping depends on auditory experience. The Journal of the Acoustical Society of America, 124(4), 2263-2271.

4. Molnar, M., Lallier, M., & Carreiras, M. (2014). The amount of language exposure determines nonlinguistic tone grouping biases in infants from a bilingual environment. Language Learning, 64(s2), 45-64.

5. Molnar, M., Carreiras, M., & Gervain, J. (2016). Language dominance shapes non-linguistic rhythmic grouping in bilinguals. Cognition, 152, 150-159.

6. Ross, J. M., & Hamm, J. P. (2020). Cortical microcircuit mechanisms of mismatch negativity and its underlying subcomponents. Frontiers in Neural Circuits, 14, 13.

7. Simon, J., Balla, V., & Winkler, I. (2019). Temporal boundary of auditory event formation: An electrophysiological marker. International Journal of Psychophysiology, 140, 53-61.

8. Studenova, A. A., Forster, C., Engemann, D. A., Hensch, T., Sander, C., Mauche, N., ... & Nikulin, V. V. (2023). Event-related modulation of alpha rhythm explains the auditory P300 evoked response in EEG. bioRxiv, 2023-02.

9. Yoshida, K. A., Iversen, J. R., Patel, A. D., Mazuka, R., Nito, H., Gervain, J., & Werker, J. F. (2010). The development of perceptual grouping biases in infancy: A Japanese-English cross-linguistic study. Cognition, 115(2), 356-361.

10. Zhang, Y., Yan, F., Wang, L., Wang, Y., Wang, C., Wang, Q., & Huang, L. (2018). Cortical areas associated with mismatch negativity: A connectivity study using propofol anesthesia. Frontiers in Human Neuroscience, 12, 392.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The image analysis pipeline is tested in analysing microscopy imaging data of gastruloids of varying sizes, for which an optimised protocol for in toto image acquisition is established based on whole mount sample preparation using an optimal refractive index matched mounting media, opposing dual side imaging with two-photon microscopy for enhanced laser penetration, dual view registration, and weighted fusion for improved in toto sample data representation. For enhanced imaging speed in a two-photon microscope, parallel imaging was used, and the authors performed spectral unmixing analysis to avoid issues of signal cross-talk.

In the image analysis pipeline, different pre-treatments are done depending on the analysis to be performed (for nuclear segmentation - contrast enhancement and normalisation; for quantitative analysis of gene expression - corrections for optical artifacts inducing signal intensity variations). Stardist3D was used for the nuclear segmentation. The study analyses into properties of gastruloid nuclear density, patterns of cell division, morphology, deformation, and gene expression.

Strengths:

The methods developed are sound, well described, and well-validated, using a sample challenging for microscopy, gastruloids. Many of the established methods are very useful (e.g. registration, corrections, signal normalisation, lazy loading bioimage visualisation, spectral decomposition analysis), facilitate the development of quantitative research, and would be of interest to the wider scientific community.

We thank the reviewer for this positive feedback.

Weaknesses:

A recommendation should be added on when or under which conditions to use this pipeline.

We thank the reviewer for this valuable feedback, which will be addressed in the revision. In general, the pipeline is applicable to any tissue, but it is particularly useful for large and dense 3D samples—such as organoids, embryos, explants, spheroids, or tumors—that are typically composed of multiple cell layers and have a thickness greater than 50 µm.

The processing and analysis pipeline are compatible with any type of 3D imaging data (e.g. confocal, 2 photon, light-sheet, live or fixed).

- Spectral unmixing to remove signal cross-talk of multiple fluorescent targets is typically more relevant in two-photon imaging due to the broader excitation spectra of fluorophores compared to single-photon imaging. In confocal or light-sheet microscopy, alternating excitation wavelengths often circumvents the need for unmixing. Spectral decomposition performs even better with true spectral detectors; however, these are usually not non-descanned detectors, which are more appropriate for deep tissue imaging. Our approach demonstrates that simultaneous cross-talk-free four-color two-photon imaging can be achieved in dense 3D specimen with four non-descanned detectors and co-excitation by just two laser lines. Depending on the dispersion in optically dense samples, depth-dependent apparent emission spectra need to be considered.

- Nuclei segmentation using our trained StarDist3D model is applicable to any system under two conditions: (1) the nuclei exhibit a star-convex shape, as required by the StarDist architecture, and (2) the image resolution is sufficient in XYZ to allow resampling. The exact sampling required is object- and system-dependent, but the goal is to achieve nearly isotropic objects with diameters of approximately 15 pixels while maintaining image quality. In practice, images containing objects that are natively close to or larger than 15 pixels in diameter should segment well after resampling. Conversely, images with objects that are significantly smaller along one or more dimensions will require careful inspection of the segmentation results.

- Normalization is broadly applicable to multicolor data when at least one channel is expected to be ubiquitously expressed within its domain. Wavelength-dependent correction requires experimental calibration using either an ubiquitous signal at each wavelength. Importantly, this calibration only needs to be performed once for a given set of experimental conditions (e.g., fluorophores, tissue type, mounting medium).

- Multi-scale analysis of gene expression and morphometrics is applicable to any 3D multicolor image. This includes both the 3D visualization tools (Napari plugins) and the various analytical plots (e.g., correlation plots, radial analysis). Multi-scale analysis can be performed even with imperfect segmentation, as long as segmentation errors tend to cancel out when averaged locally at the relevant spatial scale. However, systematic errors—such as segmentation uncertainty along the Z-axis due to strong anisotropy—may accumulate and introduce bias in downstream analyses. Caution is advised when analyzing hollow structures (e.g., curved epithelial monolayers with large cavities), as the pipeline was developed primarily for 3D bulk tissues, and appropriate masking of cavities would be needed.

Reviewer #2 (Public review):

Summary:

This study presents an integrated experimental and computational pipeline for high-resolution, quantitative imaging and analysis of gastruloids. The experimental module employs dual-view two-photon spectral imaging combined with optimized clearing and mounting techniques to image whole-mount immunostained gastruloids. This approach enables the acquisition of comprehensive 3D images that capture both tissue-scale and single-cell level information.

The computational module encompasses both pre-processing of acquired images and downstream analysis, providing quantitative insights into the structural and molecular characteristics of gastruloids. The pre-processing pipeline, tailored for dual-view two-photon microscopy, includes spectral unmixing of fluorescence signals using depth-dependent spectral profiles, as well as image fusion via rigid 3D transformation based on content-based block-matching algorithms. Nuclei segmentation was performed using a custom-trained StarDist3D model, validated against 2D manual annotations, and achieving an F1 score of 85+/-3% at a 50% intersection-over-union (IoU) threshold. Another custom-trained StarDist3D model enabled accurate detection of proliferating cells and the generation of 3D spatial maps of nuclear density and proliferation probability. Moreover, the pipeline facilitates detailed morphometric analysis of cell density and nuclear deformation, revealing pronounced spatial heterogeneities during early gastruloid morphogenesis.

All computational tools developed in this study are released as open-source, Python-based software.

Strengths:

The authors applied two-photon microscopy to whole-mount deep imaging of gastruloids, achieving in toto visualization at single-cell resolution. By combining spectral imaging with an unmixing algorithm, they successfully separated four fluorescent signals, enabling spatial analysis of gene expression patterns.

The entire computational workflow, from image pre-processing to segmentation with a custom-trained StarDist3D model and subsequent quantitative analysis, is made available as open-source software. In addition, user-friendly interfaces are provided through the open-source, community-driven Napari platform, facilitating interactive exploration and analysis.

We thank the reviewer for this positive feedback.

Weaknesses:

The computational module appears promising. However, the analysis pipeline has not been validated on datasets beyond those generated by the authors, making it difficult to assess its general applicability.

We agree that applying our analysis pipeline to published datasets—particularly those acquired with different imaging systems—would be valuable. However, only a few high-resolution datasets of large organoid samples are publicly available, and most of these either lack multiple fluorescence channels or represent 3D hollow structures. Our computational pipeline consists of several independent modules: spectral filtering, dual-view registration, local contrast enhancement, 3D nuclei segmentation, image normalization based on a ubiquitous marker, and multiscale analysis of gene expression and morphometrics.

Spectral filtering has already been applied in other systems (e.g. [7] and [8]), but is here extended to account for imaging depth-dependent apparent emission spectra of the different fluorophores. In our pipeline, we provide code to run spectral filtering on multichannel images, integrated in Python. In order to apply the spectral filtering algorithm utilized here, spectral patterns of each fluorophore need to be calibrated as a function of imaging depth, which depend on the specific emission windows and detector settings of the microscope.

Image normalization using a wavelength-dependent correction also requires calibration on a given imaging setup to measure the difference in signal decay among the different fluorophores species. To our knowledge, the calibration procedures for spectral-filtering and our image-normalization approach have not been performed previously in 3D samples, which is why validation on published datasets is not readily possible. Nevertheless, they are described in detail in the Methods section, and the code used—from the calibration measurements to the corrected images—is available open-source at the Zenodo link in the manuscript.

Dual-view registration, local contrast enhancement, and multiscale analysis of gene expression and morphometrics are not limited to organoid data or our specific imaging modalities. If we identify suitable datasets to validate these modules, we will include them in the revised manuscript.

To evaluate our 3D nuclei segmentation model, we plan to test it on diverse systems, including gastruloids stained with the nuclear marker Draq5 from Moos et al. [1]; breast cancer spheroids; primary ductal adenocarcinoma organoids; human colon organoids and HCT116 monolayers from Ong et al. [2]; and zebrafish tissues imaged by confocal microscopy from Li et al [3]. These datasets were acquired using either light-sheet or confocal microscopy, with varying imaging parameters (e.g., objective lens, pixel size, staining method).

Preliminary results are promising (see Author response image 1). We will provide quantitative comparisons of our model’s performance on these datasets, using annotations or reference predictions provided by the original authors where available.

Author response image 1.

Qualitative comparison of our custom Stardist3D segmentation strategy on diverse published 3D nuclei datasets. We show one slice from the XY plane for simplicity. (a) Gastruloid stained with the nuclear marker DRAQ5 imaged with an open-top dual-view and dual-illumination LSM [1]. (b) Breast cancer spheroid [2]. (c) Primary pancreatic ductal adenocarcinoma organoids imaged with confocal microscopy[2]. (d) Human colon organoid imaged with LSM laser scanning confocal microscope [2]. (e) Monolayer HCT116 cells imaged with LSM laser scanning confocal microscope [2]. (f) Fixed zebrafish embryo stained for nuclei and imaged with a Zeiss LSM 880 confocal microscopy [3].

Besides, the nuclei segmentation component lacks benchmarking against existing methods.

We agree with the reviewer that a benchmark against existing segmentation methods would be very useful. We tried different pre-trained models:

- CellPose, which we tested in a previous paper ([4]) and which showed poor performances compared to our trained StarDist3D model.

- DeepStar3D ([2]) is only available in the software 3DCellScope. We could not benchmark the model on our data, because the free and accessible version of the software is limited to small datasets. An image of a single whole-mount gastruloid with one channel, having dimensions (347,467,477) was too large to be processed, see screenshot below. The segmentation model could not be extracted from the source code and tested externally because the trained DeepStar3D weights are encrypted.

Author response image 2.

Screenshot of the 3DCellScore software. We could not perform 3D nuclei segmentation of a whole-mount gastruloids because the image size was too large to be processed.

- AnyStar ([5]), which is a model trained from the StarDist3D architecture, was not performing well on our data because of the heterogeneous stainings. Basic pre-processing such as median and gaussian filtering did not improve the results and led to wrong segmentation of touching nuclei. AnyStar was demonstrated to segment well colon organoids in Ong et al, 2025 ([2]), but the nuclei were more homogeneously stained. Our Hoechst staining displays bright chromatin spots that are incorrectly labeled as individual nuclei.

- Cellos ([6]), another model trained from StarDist3D, was also not performing well. The objects used for training and to validate the results are sparse and not touching, so the predicted segmentation has a lot of false negatives even when lowering the probability threshold to detect more objects. Additionally, the network was trained with an anisotropy of (9,1,1), based on images with low z resolution, so it performed poorly on almost isotropic images. Adapting our images to the network’s anisotropy results in an imprecise segmentation that can not be used to measure 3D nuclei deformations.

We tried both Cellos and AnyStar predictions on a gastruloid image from Fig. S2 of our main manuscript. Author response image 3 displays the results qualitatively compared to our trained model Stardist-tapenade. For the revision of the paper, we will perform a comprehensive benchmark of these state-of-the-art routines, including quantitative assessment of the performance.

Author response image 3.

Qualitative comparison of two published segmentation models versus our model. We show one slice from the XY plane for simplicity. Segmentations are displayed with their contours only. (Top left) Gastruloid stained with Hoechst, image extracted from Fig S2 of our manuscript. (Top right) Same image overlayed with the prediction from the Cellos model, showing many false negatives. (Bottom left) Same image overlayed with the prediction from our Stardist-tapenade model. (Bottom right) Same image overlayed with the prediction from the AnyStar model, false positives are indicated with a red arrow.

Appraisal:

The authors set out to establish a quantitative imaging and analysis pipeline for gastruloids using dual-view two-photon microscopy, spectral unmixing, and a custom computational framework for 3D segmentation and gene expression analysis. This aim is largely achieved. The integration of experimental and computational modules enables high-resolution in toto imaging and robust quantitative analysis at the single-cell level. The data presented support the authors' conclusions regarding the ability to capture spatial patterns of gene expression and cellular morphology across developmental stages.

Impact and utility:

This work presents a compelling and broadly applicable methodological advance. The approach is particularly impactful for the developmental biology community, as it allows researchers to extract quantitative information from high-resolution images to better understand morphogenetic processes. The data are publicly available on Zenodo, and the software is released on GitHub, making them highly valuable resources for the community.

We thank the reviewer for these positive feedbacks.

Reviewer #3 (Public review):

Summary

The paper presents an imaging and analysis pipeline for whole-mount gastruloid imaging with two-photon microscopy. The presented pipeline includes spectral unmixing, registration, segmentation, and a wavelength-dependent intensity normalization step, followed by quantitative analysis of spatial gene expression patterns and nuclear morphometry on a tissue level. The utility of the approach is demonstrated by several experimental findings, such as establishing spatial correlations between local nuclear deformation and tissue density changes, as well as the radial distribution pattern of mesoderm markers. The pipeline is distributed as a Python package, notebooks, and multiple napari plugins.

Strengths

The paper is well-written with detailed methodological descriptions, which I think would make it a valuable reference for researchers performing similar volumetric tissue imaging experiments (gastruloids/organoids). The pipeline itself addresses many practical challenges, including resolution loss within tissue, registration of large volumes, nuclear segmentation, and intensity normalization. Especially the intensity decay measurements and wavelength-dependent intensity normalization approach using nuclear (Hoechst) signal as reference are very interesting and should be applicable to other imaging contexts. The morphometric analysis is equally well done, with the correlation between nuclear shape deformation and tissue density changes being an interesting finding. The paper is quite thorough in its technical description of the methods (which are a lot), and their experimental validation is appropriate. Finally, the provided code and napari plugins seem to be well done (I installed a selected list of the plugins and they ran without issues) and should be very helpful for the community.

We thank the reviewer for his positive feedback and appreciation of our work.

Weaknesses

I don't see any major weaknesses, and I would only have two issues that I think should be addressed in a revision:

(1) The demonstration notebooks lack accompanying sample datasets, preventing users from running them immediately and limiting the pipeline's accessibility. I would suggest to include (selective) demo data set that can be used to run the notebooks (e.g. for spectral unmixing) and or provide easily accessible demo input sample data for the napari plugins (I saw that there is some sample data for the processing plugin, so this maybe could already be used for the notebooks?).

We thank the reviewer for this relevant suggestion. The 7 notebooks were updated to automatically download sample tests. The different parts of the pipeline can now be run immediately: https://github.com/GuignardLab/tapenade/tree/chekcs_on_notebooks/src/tapenade/notebooks

(2) The results for the morphometric analysis (Figure 4) seem to be only shown in lateral (xy) views without the corresponding axial (z) views. I would suggest adding this to the figure and showing the density/strain/angle distributions for those axial views as well.

We agree with the reviewer that a morphometric analysis based on the axial views would be informative and plan to perform this analysis for the revision.

(1) Moos, F., Suppinger, S., de Medeiros, G., Oost, K.C., Boni, A., Rémy, C., Weevers, S.L., Tsiairis, C., Strnad, P. and Liberali, P., 2024. Open-top multisample dual-view light-sheet microscope for live imaging of large multicellular systems. Nature Methods, 21(5), pp.798-803.

(2) Ong, H.T., Karatas, E., Poquillon, T., Grenci, G., Furlan, A., Dilasser, F., Mohamad Raffi, S.B., Blanc, D., Drimaracci, E., Mikec, D. and Galisot, G., 2025. Digitalized organoids: integrated pipeline for high-speed 3D analysis of organoid structures using multilevel segmentation and cellular topology. Nature Methods, 22(6), pp.1343-1354.

(3) Li, L., Wu, L., Chen, A., Delp, E.J. and Umulis, D.M., 2023. 3D nuclei segmentation for multi-cellular quantification of zebrafish embryos using NISNet3D. Electronic Imaging, 35, pp.1-9.

(4) Vanaret, J., Dupuis, V., Lenne, P. F., Richard, F., Tlili, S., & Roudot, P. (2023). A detector-independent quality score for cell segmentation without ground truth in 3D live fluorescence microscopy. IEEE Journal of Selected Topics in Quantum Electronics, 29(4: Biophotonics), 1-12.

(5) Dey, N., Abulnaga, M., Billot, B., Turk, E. A., Grant, E., Dalca, A. V., & Golland, P. (2024). AnyStar: Domain randomized universal star-convex 3D instance segmentation. In Proceedings of the IEEE/CVF Winter Conference on Applications of Computer Vision (pp. 7593-7603).

(6) Mukashyaka, P., Kumar, P., Mellert, D. J., Nicholas, S., Noorbakhsh, J., Brugiolo, M., ... & Chuang, J. H. (2023). High-throughput deconvolution of 3D organoid dynamics at cellular resolution for cancer pharmacology with Cellos. Nature Communications, 14(1), 8406.

(7) Rakhymzhan, A., Leben, R., Zimmermann, H., Günther, R., Mex, P., Reismann, D., ... & Niesner, R. A. (2017). Synergistic strategy for multicolor two-photon microscopy: application to the analysis of germinal center reactions in vivo. Scientific reports, 7(1), 7101.

(8) Dunsing, V., Petrich, A., & Chiantia, S. (2021). Multicolor fluorescence fluctuation spectroscopy in living cells via spectral detection. Elife, 10, e69687.

Author response:

Reviewer #1 (Public Review):

(1) Figure 3: it is unclear what is the efficiency of Msi2 deletion shRNA - could you demonstrate it by at least two independent methods? (QPCR, Western, or IHC?) please quantitate the data.

In Figure 3, we did not delete Msi2 via shRNA. Instead, we utilized a genetic model in which the Msi2 gene was disrupted via gene trap mutagenesis. We have also used this model in previous publications to define the impact of Msi2 loss in other systems1.

(2) In Figure 4, similarly, it is unclear if Msi2 depletion was effective- and what is shRNA efficiency. Please test this by at least two independent methods (QPCR, Western, or IHC) and also please quantitate the data

We demonstrated that the efficiency of Msi2 depletion was ~83% (Figures 4A and 4C) via qPCR analysis for our in vitro and in vivo experiments, respectively, and verified the knockdown via bulk RNA-seq analysis. The shRNA hairpin used was previously validated and published by our lab2.

(3) the reason for impairment of cell growth demonstrated in Figs 3 and 4 is not clear: is it apoptosis? Necrosis? Cell cycle defects? Autophagy? Senescence? Please probe 2-3 possibilities and provide the data.

The basis of the cell growth impairment after Msi2 deletion/knockdown in this paper is certainly an important question, and future experiments will be performed to better delineate this. In previous publications loss of Msi2 in leukemia cells has been shown to inhibit growth via arrested cell cycle progression by increasing the expression of p213. Further, loss of Msi2 was also shown to promote apoptosis in part by upregulating Bax3. These data suggest that Msi2 can have an impact via multiple distinct mechanisms including by mediating cell cycle arrest and blocking apoptosis. While these specific genes were not detectably changed after loss of Msi2 in lung cancer cells, other genes in these and other pathways will be important to study in the future.

(4) Since Musashi-1 is a Musashi-2 paralogue that could compensate for Musashi-2 loss, please test Msi1 expression levels in matching Fig 3 and Fig 4 sections (in cells/ tumors with Msi2 deletion and in KP cells with Msi2 shRNA). One method could suffice here.

In our RNA-seq of cells following Msi2 knockdown, Msi1 expression was undetectable. The TPM values for Msi1 in control and knockdown cells were less than 0.01, suggesting that it did not compensate for the loss of Msi2.

(5) It is not exactly clear why RNA-seq (as opposed to proteomics) was done to investigate downstream Msi2 targets (since Msi2 is in first place, translational and not transcriptional regulator)- . RNA effects in Fig 5J are quite modest, 2-fold or so. It would be useful (if antibodies available) to test four targets in Fig 5J by Western blot, to see any impact of musashi-2 depletion on those target protein levels. Indeed, several papers - including Kudinov et al PNAS, PMID: 27274057, Makhov P et al PMID: 33723247 and PMID: 37173995 - used proteomics/ RIP approaches and found direct Musashi-2 targets in lung cancer, including EGFR, and others.

Previous published work from the lab showed that expression of Msi2 in the context of myeloid leukemia1can not only repress NUMB protein (I believe protein should be all caps?) (as has been previously demonstrated in the nervous system) but also Numb RNA. This indicated that as an RNA binding protein, Msi2 also can bind and destabilize direct binding targets such as Numb; this was the reason for pursuing transcriptomic analysis.  However as the reviewer suggests, proteomic studies are certainly very important to develop a complete picture of the impact of Musashi to determine which targets are controlled by Msi2 at the protein level.

Reviewer #2 (Public Review):

(1) It will be interesting to determine whether Msi2+ cells are a relatively stable subset or rather the Msi2+ cells in lung is a dynamic concept that is transient or interconvertible. This is relevant to the interpretation of what Msi2 positivity really means.

In previous unpublished work from our lab, we have found that Msi2+ cells from a GFP reporter KPf/fC mouse are readily able to become GFP negative (Msi2-), but the inverse is not true. Specifically, when Msi2+ KPf/fC pancreatic cells were transplanted into the flanks of NSG mice, Msi2+ cells formed tumors in all recipients; these tumors contained both GFP+ and GFP- cells (over 80%)  recapitulating the original heterogeneity and suggesting GFP+ cells can give rise to both GFP+ and GFP- cells (Lytle and Reya, unpublished observations). In contrast only a small subset of GFP- transplanted mice formed tumors. One of the rare GFP- derived tumors was isolated and found to contain largely GFP- cells, with ~0.1% GFP+ cells. The small frequency of GFP expression could be from contaminating cells or may suggest that GFP- cells retain some ability to switch on Msi under selective pressure, and that although they pose a lower risk of driving tumorigenesis than Msi+ cells, they may nonetheless bear latent potential to become higher risk. These data may offer a possible model for projecting the potential of Msi2+ cells in the lung, but is something that needs to be further studied in this tissue.

(2) Does Kras mutation and/or p53 loss upregulate Msi2? This point and the point above are related to whether Msi2+ cells are truly more susceptible to tumorigenesis, as the authors suggested.

In unpublished work from our lab, we have found that Kras mutation upregulates Msi2 over baseline and subsequent p53 loss upregulates Msi2 further in the context of pancreatic cells (Lytle and Reya unpublished results), therefore it is possible that the same is true for the lung. Specifically, we have observed that Msi2 increased from normal acinar cells to Kras-mutated acinar (e.g. pancreatic intraepithelial neoplasia (PanIN)).

To address whether Msi2+ cells are more susceptible to tumorigenesis, we have recently published data showing that the stabilization of the oncogenic MYC protein in lung Msi2+ cells drive the formation of small-cell lung cancer in a new inducible Msi2-CreERT2; CAG-LSL-MycT58A mice (Msi2-Myc)4 model. More importantly, this data provides the first evidence that normal Msi2+ cells are primed and highly sensitive to MYC-driven transformation across many organs and not just the lung4.

(3) The KO of Msi2 reducing tumor number and burden in the lung cancer initiation model is interesting. However, there are two alternative interpretations. First, it is possible that the Msi2 KO mice (without Kras activation and p53 loss) has reduced total lung cell numbers or altered percentage of stem cells. There is currently only one sentence citing data not shown on line 125, commenting that there is no difference in BASC and AT2 cell populations. It will be helpful that such data are shown and the effect of KO on overall lung mass or cellularity is clarified. Second, the phenotype may also be due to a difference in the efficiencies of cre on Kras and p53 in the Msi2 WT and KO mice.

We isolated the lungs of three Msi2 WT and three Msi2 KO mice and used immunofluorescence staining to stain for CC10 (BASC) and SPC (AT2) to determine if these cell populations were reduced after Msi2 loss alone. Below are representative images showing that the Msi2 KO mice did not have lower numbers of both BASC and AT2 cell populations. 

Author response image 1.

(4) All shRNA experiments (for both Msi2 KD and the KD of candidate genes) utilized a single shRNA. This approach cannot exclude off-target effects of the shRNA.

The shRNA hairpin used for Msi2 was previously validated and published by our lab2. Additionally, in this work we did develop and use a Msi2 genetic knockout mouse model that validates our shRNA knockdown data showing the specific impact of Msi2 on lung tumor growth.

(5) The technical details of the PDX experiment (Figure 4F) are not fully explained.

Due to space considerations, we were unable not put the specifics in the legend, but the details are in the methods section (Flank Transplant Assays). In brief, 500,000 cells/well were plated in a 6-well plate coated with Matrigel and 83,000 cells/well were plated in a 24-well plate coated with Matrigel for subsequent determination of transduction efficiency via FACS. 24 hours after transduction, media from the cells was collected and placed on ice. 1mL of 2mg/mL collagenase/dispase was then added to the well and incubated for 45 minutes at 37ºC to dissociate the remaining cells from Matrigel followed by subsequent washes. Cells were pelleted by centrifugation and an equivalent number of shControl and shMsi2 transduced cells were resuspended in full media, mixed at a 1:1 ratio with growth factor reduced Matrigel at a final volume of 100 μL, and transplanted subcutaneously into the flanks of NSG recipient mice.

Reviewer #3 (Public Review):

- In Figure 1, characterization of Msi2 expression in the normal mouse lung was carried out by using a Msi2-GFP Knock-in reporter and analyzed by flow cytometry followed by cytospins and immunostaining. Additional characterization of Msi2 expression by co-immunostaining with well-known markers of airway and alveolar cell types in intact lung tissue will strengthen the existing data and provide more specific information about Msi2 expression and abundancy in relevant cell types. It will be also interesting to know whether Msi2 is expressed or not in other abundant lung cell types such as ciliated and AT1 cells.

We performed co-staining of Msi2 and CC10 as well as Msi2 and SPC in Figure 1C. In the future we can include additional markers as well as markers for airway and other alveolar cell types.

- While this set of experiments provide strong evidence that Msi2 is required for tumor progression and growth in lung adenocarcinoma, it is unclear whether normal Msi2+ lung cells are more responsive to transformation or whether Msi2 is upregulated early during the process of tumorigenesis. Future lineage tracing experiments using Msi2-CreER and mouse models of chemically-induced lung carcinogenesis will provide additional data that will fully support this claim.

Recently, we published data showing that Msi2 is expressed in Clara cells at the bronchoalveolar junction in the lung of our new Msi2-CreERT2 knock-in mouse model4. Furthermore, stabilization of the oncogenic MYC protein in these specific cells to model Myc amplification was sufficient to drive the formation of small-cell lung cancer4. These data excitingly demonstrate that Msi2+ cells are more responsive to transformation after Myc stabilization.

- In Figure 4F, Patient-derived xenograft (PDX) assays were conducted in 2 patients only and the percentage of cells infected by shRNA-Msi2 is low in both PDX (30% and 10% for patient 1 and 2 respectively). It is surprising that Msi2 downregulation in a small percentage of tumor cells has such a dramatic effect on tumor growth and expansion. Confirmation of this finding with additional patient samples would suggest an important non-cell autonomous role for Msi2 in lung adenocarcinoma.

In the future we hope to collect more patient samples to further validate the data presented with the first 2 patients shown here. We are not certain about the reason behind the large impact of Msi2 inhibition, but as cancer stem cells drive the formation of the rest of the tumor and also drive the stromal microenvironment, it is possible that when Msi2 is deleted, Msi2- cells no longer form tumors? and also the ability to build the stromal microenvironment is impacted. This possibility needs to be further tested in future experiments.

References

(1) Ito, T. Kwon, H. Y., Zimdahl, B., Congdon, K. L., Blum, J., Lento, W. E., Zhao, C., Lagoo, A., Gerrard, G., Foroni, L., Goldman, J., Goh, H., Kim, S. H., Kim, D. W., Chuah, C., Oehler, V. G., Radich, J. P., Jordan, C. T., & Reya, T. Regulation of myeloid leukaemia by the cell-fate determinant Musashi. Nature 466, 765–768 (2010).

(2) Fox, R. G. Lytle, N. K., Jaquish, D. V., Park, F. D., Ito, T., Bajaj, J., Koechlein, C. S., Zimdahl, B., Yano, M., Kopp, J. L., Kritzik, M., Sicklick, J. K., Sander, M., Grandgenett, P. M., Hollingsworth, M. A., Shibata, S., Pizzo, D., Valasek, M. A., Sasik, R., Scadeng, M., Okano, H., Kim, Y., MacLeod, A. R., Lowy, A. M., & Reya, T. Image-based detection and targeting of therapy resistance in pancreatic adenocarcinoma. Nature 534, 407–411 (2016).

(3) Zhang, H. Tan, S., Wang, J., Chen, S., Quan, J., Xian, J., Zhang, Ss., He, J., & Zhang, L. Musashi2 modulates K562 leukemic cell proliferation and apoptosis involving the MAPK pathway. Exp Cell Res 320, 119-27 (2014).

(4) Rajbhandari, N., Hamilton, M., Quintero, C.M., Ferguson, L.P., Fox, R., Schürch, C.M., Wang, J., Nakamura, M., Lytle, N.K., McDermott, M., Diaz, E., Pettit, H., Kritzik, M., Han, H., Cridebring, D., Wen, K.W., Tsai, S., Goggins, M.G., Lowy, A.M., Wechsler-Reya, R.J., Von Hoff, D.D., Newman, A.M., & Reya, T. Single-cell mapping identifies MSI+ cells as a common origin for diverse subtypes of pancreatic cancer. Cancer Cell 41(11):1989-2005.e9 (2023).

Author Response

eLife assessment

This study presents potentially valuable results on glutamine-rich motifs in relation to protein expression and alternative genetic codes. The author's interpretation of the results is so far only supported by incomplete evidence, due to a lack of acknowledgment of alternative explanations, missing controls and statistical analysis and writing unclear to non experts in the field. These shortcomings could be at least partially overcome by additional experiments, thorough rewriting, or both.

We thank both the Reviewing Editor and Senior Editor for handling this manuscript and will submit our revised manuscript after the reviewed preprint is published by eLife.  

Reviewer #1 (Public Review):

Summary

This work contains 3 sections. The first section describes how protein domains with SQ motifs can increase the abundance of a lacZ reporter in yeast. The authors call this phenomenon autonomous protein expression-enhancing activity, and this finding is well supported. The authors show evidence that this increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance, and that this phenomenon is not affected by mutants in translational quality control. It was not completely clear whether the increased protein abundance is due to increased translation or to increased protein stability.

In section 2, the authors performed mutagenesis of three N-terminal domains to study how protein sequence changes protein stability and enzymatic activity of the fusions. These data are very interesting, but this section needs more interpretation. It is not clear if the effect is due to the number of S/T/Q/N amino acids or due to the number of phosphorylation sites.

In section 3, the authors undertake an extensive computational analysis of amino acid runs in 27 species. Many aspects of this section are fascinating to an expert reader. They identify regions with poly-X tracks. These data were not normalized correctly: I think that a null expectation for how often poly-X track occur should be built for each species based on the underlying prevalence of amino acids in that species. As a result, I believe that the claim is not well supported by the data.

Strengths

This work is about an interesting topic and contains stimulating bioinformatics analysis. The first two sections, where the authors investigate how S/T/Q/N abundance modulates protein expression level, is well supported by the data. The bioinformatics analysis of Q abundance in ciliate proteomes is fascinating. There are some ciliates that have repurposed stop codons to code for Q. The authors find that in these proteomes, Q-runs are greatly expanded. They offer interesting speculations on how this expansion might impact protein function.

Weakness

At this time, the manuscript is disorganized and difficult to read. An expert in the field, who will not be distracted by the disorganization, will find some very interesting results included. In particular, the order of the introduction does not match the rest of the paper.

In the first and second sections, where the authors investigate how S/T/Q/N abundance modulates protein expression levels, it is unclear if the effect is due to the number of phosphorylation sites or the number of S/T/Q/N residues.

There are three reasons why the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities:

First, we have reported previously that phosphorylation-defective Rad51-NTD (Rad51-3SA) and wild-type Rad51-NTD exhibit similar autonomous PEE activity. Mec1/Tel1-dependent phosphorylation of Rad51-NTD antagonizes the proteasomal degradation pathway, increasing the half-life of Rad51 from ∼30 min to ≥180 min (Ref 27; Woo, T. T. et al. 2020).

1. T. T. Woo, C. N. Chuang, M. Higashide, A. Shinohara, T. F. Wang, Dual roles of yeast Rad51 N-terminal domain in repairing DNA double-strand breaks. Nucleic Acids Res 48, 8474-8489 (2020).

Second, in our preprint manuscript, we have also shown that phosphorylation-defective Rad53-SCD1 (Rad51-SCD1-5STA) also exhibits autonomous PEE activity similar to that of wild-type Rad53-SCD (Figure 2D, Figure 4A and Figure 4C).

Third, as revealed by the results of our preprint manuscript (Figure 4), it is the percentages, and not the numbers, of S/T/Q/N residues that are correlated with the PEE activities of Q-rich motifs.

The authors also do not discuss if the N-end rule for protein stability applies to the lacZ reporter or the fusion proteins.

The autonomous PEE function of S/T/Q-rich NTDs is unlikely to be relevant to the N-end rule. The N-end rule links the in vivo half-life of a protein to the identity of its N-terminal residues. In S. cerevisiae, the N-end rule operates as part of the ubiquitin system and comprises two pathways. First, the Arg/N-end rule pathway, involving a single N-terminal amidohydrolase Nta1, mediates deamidation of N-terminal asparagine (N) and glutamine (Q) into aspartate (D) and glutamate (E), which in turn are arginylated by a single Ate1 R-transferase, generating the Arg/N degron. N-terminal R and other primary degrons are recognized by a single N-recognin Ubr1 in concert with ubiquitin-conjugating Ubc2/Rad6. Ubr1 can also recognize several other N-terminal residues, including lysine (K), histidine (H), phenylalanine (F), tryptophan (W), leucine (L) and isoleucine (I) (Bachmair, A. et al. 1986; Tasaki, T. et al. 2012; Varshavshy, A. et al. 2019). Second, the Ac/N-end rule pathway targets proteins containing N-terminally acetylated (Ac) residues. Prior to acetylation, the first amino acid methionine (M) is catalytically removed by Met-aminopeptides, unless a residue at position 2 is non-permissive (too large) for MetAPs. If a retained N-terminal M or otherwise a valine (V), cysteine (C), alanine (A), serine (S) or threonine (T) residue is followed by residues that allow N-terminal acetylation, the proteins containing these AcN degrons are targeted for ubiquitylation and proteasome-mediated degradation by the Doa10 E3 ligase (Hwang, C. S., 2019).

A. Bachmair, D. Finley, A. Varshavsky, In vivo half-life of a protein is a function of its amino-terminal residue. Science 234, 179-186 (1986).

T. Tasaki, S. M. Sriram, K. S. Park, Y. T. Kwon, The N-end rule pathway. Annu Rev Biochem 81, 261-289 (2012).

A. Varshavsky, N-degron and C-degron pathways of protein degradation. Proc Natl Acad Sci 116, 358-366 (2019).

C. S. Hwang, A. Shemorry, D. Auerbach, A. Varshavsky, The N-end rule pathway is mediated by a complex of the RING-type Ubr1 and HECT-type Ufd4 ubiquitin ligases. Nat Cell Biol 12, 1177-1185 (2010).

The PEE activities of these S/T/Q-rich domains are unlikely to arise from counteracting the N-end rule for two reasons. First, the first two amino acid residues of Rad51-NTD, Hop1-SCD, Rad53-SCD1, Sup35-PND, Rad51-ΔN, and LacZ-NVH are MS, ME, ME, MS, ME, and MI, respectively, where M is methionine, S is serine, E is glutamic acid and I is isoleucine. Second, Sml1-NTD behaves similarly to these N-terminal fusion tags, despite its methionine and glutamine (MQ) amino acid signature at the N-terminus.

The most interesting part of the paper is an exploration of S/T/Q/N-rich regions and other repetitive AA runs in 27 proteomes, particularly ciliates. However, this analysis is missing a critical control that makes it nearly impossible to evaluate the importance of the findings. The authors find the abundance of different amino acid runs in various proteomes. They also report the background abundance of each amino acid. They do not use this background abundance to normalize the runs of amino acids to create a null expectation from each proteome. For example, it has been clear for some time (Ruff, 2017; Ruff et al., 2016) that Drosophila contains a very high background of Q's in the proteome and it is necessary to control for this background abundance when finding runs of Q's.

We apologize for not explaining sufficiently well the topic eliciting this reviewer’s concern in our preprint manuscript. In the second paragraph of page 14, we cite six references to highlight that SCDs are overrepresented in yeast and human proteins involved in several biological processes (32, 74), and that polyX prevalence differs among species (43, 75-77).

1. Cheung HC, San Lucas FA, Hicks S, Chang K, Bertuch AA, Ribes-Zamora A. An S/T-Q cluster domain census unveils new putative targets under Tel1/Mec1 control. BMC Genomics. 2012;13:664.

2. Mier P, Elena-Real C, Urbanek A, Bernado P, Andrade-Navarro MA. The importance of definitions in the study of polyQ regions: A tale of thresholds, impurities and sequence context. Comput Struct Biotechnol J. 2020;18:306-13.

3. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

4. Kuspa A, Loomis WF. The genome of Dictyostelium discoideum. Methods Mol Biol. 2006;346:15-30.

5. Davies HM, Nofal SD, McLaughlin EJ, Osborne AR. Repetitive sequences in malaria parasite proteins. FEMS Microbiol Rev. 2017;41(6):923-40.

6. Mier P, Alanis-Lobato G, Andrade-Navarro MA. Context characterization of amino acid homorepeats using evolution, position, and order. Proteins. 2017;85(4):709-19.

We will cite the two references by Kiersten M. Ruff in our revised manuscript.

K. M. Ruff and R. V. Pappu, (2015) Multiscale simulation provides mechanistic insights into the effects of sequence contexts of early-stage polyglutamine-mediated aggregation. Biophysical Journal 108, 495a.

K. M. Ruff, J. B. Warner, A. Posey and P. S. Tan (2017) Polyglutamine length dependent structural properties and phase behavior of huntingtin exon1. Biophysical Journal 112, 511a.

The authors could easily address this problem with the data and analysis they have already collected. However, at this time, without this normalization, I am hesitant to trust the lists of proteins with long runs of amino acid and the ensuing GO enrichment analysis.

Ruff KM. 2017. Washington University in St.

Ruff KM, Holehouse AS, Richardson MGO, Pappu RV. 2016. Proteomic and Biophysical Analysis of Polar Tracts. Biophys J 110:556a.

We thank Reviewer #1 for this helpful suggestion and now address this issue by means of a different approach described below.

Based on a previous study (43; Palo Mier et al. 2020), we applied seven different thresholds to seek both short and long, as well as pure and impure, polyX strings in 20 different representative near-complete proteomes, including 4X (4/4), 5X (4/5-5/5), 6X (4/6-6/6), 7X (4/7-7/7), 8-10X (≥50%X), 11-10X (≥50%X) and ≥21X (≥50%X).

To normalize the runs of amino acids and create a null expectation from each proteome, we determined the ratios of the overall number of X residues for each of the seven polyX motifs relative to those in the entire proteome of each species, respectively. The results of four different polyX motifs are shown below, i.e., polyQ (Author response image 1), polyN (Author response image 2), polyS (Author response image 3) and polyT (Author response image 4).

Author response image 1.

Q contents in 7 different types of polyQ motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 2.

N contents in 7 different types of polyN motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 3.

S contents in 7 different types of polyS motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 4.

T contents in 7 different types of polyT motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

The results summarized in these four new figures support that polyX prevalence differs among species and that the overall X contents of polyX motifs often but not always correlate with the X usage frequency in entire proteomes (43; Palo Mier et al. 2020).

Most importantly, our results reveal that, compared to Stentor coeruleus or several non-ciliate eukaryotic organisms (e.g., Plasmodium falciparum, Caenorhabditis elegans, Danio rerio, Mus musculus and Homo sapiens), the five ciliates with reassigned TAAQ and TAGQ codons not only have higher Q usage frequencies, but also more polyQ motifs in their proteomes (Figure 1). In contrast, polyQ motifs prevail in Candida albicans, Candida tropicalis, Dictyostelium discoideum, Chlamydomonas reinhardtii, Drosophila melanogaster and Aedes aegypti, though the Q usage frequencies in their entire proteomes are not significantly higher than those of other eukaryotes (Figure 1). Due to their higher N usage frequencies, Dictyostelium discoideum, Plasmodium falciparum and Pseudocohnilembus persalinus have more polyN motifs than the other 23 eukaryotes we examined here (Figure 2). Generally speaking, all 26 eukaryotes we assessed have similar S usage frequencies and percentages of S contents in polyS motifs (Figure 3). Among these 26 eukaryotes, Dictyostelium discoideum possesses many more polyT motifs, though its T usage frequency is similar to that of the other 25 eukaryotes (Figure 4).

In conclusion, these new normalized results confirm that the reassignment of stop codons to Q indeed results in both higher Q usage frequencies and more polyQ motifs in ciliates.  

Reviewer #2 (Public Review):

Summary:

This study seeks to understand the connection between protein sequence and function in disordered regions enriched in polar amino acids (specifically Q, N, S and T). While the authors suggest that specific motifs facilitate protein-enhancing activities, their findings are correlative, and the evidence is incomplete. Similarly, the authors propose that the re-assignment of stop codons to glutamine-encoding codons underlies the greater user of glutamine in a subset of ciliates, but again, the conclusions here are, at best, correlative. The authors perform extensive bioinformatic analysis, with detailed (albeit somewhat ad hoc) discussion on a number of proteins. Overall, the results presented here are interesting, but are unable to exclude competing hypotheses.

Strengths:

Following up on previous work, the authors wish to uncover a mechanism associated with poly-Q and SCD motifs explaining proposed protein expression-enhancing activities. They note that these motifs often occur IDRs and hypothesize that structural plasticity could be capitalized upon as a mechanism of diversification in evolution. To investigate this further, they employ bioinformatics to investigate the sequence features of proteomes of 27 eukaryotes. They deepen their sequence space exploration uncovering sub-phylum-specific features associated with species in which a stop-codon substitution has occurred. The authors propose this stop-codon substitution underlies an expansion of ploy-Q repeats and increased glutamine distribution.

Weaknesses:

The preprint provides extensive, detailed, and entirely unnecessary background information throughout, hampering reading and making it difficult to understand the ideas being proposed. The introduction provides a large amount of detailed background that appears entirely irrelevant for the paper. Many places detailed discussions on specific proteins that are likely of interest to the authors occur, yet without context, this does not enhance the paper for the reader.

The paper uses many unnecessary, new, or redefined acronyms which makes reading difficult. As examples:

(1) Prion forming domains (PFDs). Do the authors mean prion-like domains (PLDs), an established term with an empirical definition from the PLAAC algorithm? If yes, they should say this. If not, they must define what a prion-forming domain is formally.

The N-terminal domain (1-123 amino acids) of S. cerevisiae Sup35 was already referred to as a “prion forming domain (PFD)” in 2006 (Tuite, M. F. 2006). Since then, PFD has also been employed as an acronym in other yeast prion papers (Cox, B.S. et al. 2007; Toombs, T. et al. 2011).

M. F., Tuite, Yeast prions and their prion forming domain. Cell 27, 397-407 (2005).

B. S. Cox, L. Byrne, M. F., Tuite, Protein Stability. Prion 1, 170-178 (2007).

J. A. Toombs, N. M. Liss, K. R. Cobble, Z. Ben-Musa, E. D. Ross, [PSI+] maintenance is dependent on the composition, not primary sequence, of the oligopeptide repeat domain. PLoS One 6, e21953 (2011).

(2) SCD is already an acronym in the IDP field (meaning sequence charge decoration) - the authors should avoid this as their chosen acronym for Serine(S) / threonine (T)-glutamine (Q) cluster domains. Moreover, do we really need another acronym here (we do not).

SCD was first used in 2005 as an acronym for the Serine (S)/threonine (T)-glutamine (Q) cluster domain in the DNA damage checkpoint field (Traven, A. and Heierhorst, J. 2005). Almost a decade later, SCD became an acronym for “sequence charge decoration” (Sawle, L. et al. 2015; Firman, T. et al. 2018).

A. Traven and J, Heierhorst, SQ/TQ cluster domains: concentrated ATM/ATR kinase phosphorylation site regions in DNA-damage-response proteins. Bioessays. 27, 397-407 (2005).

L. Sawle and K, Ghosh, A theoretical method to compute sequence dependent configurational properties in charged polymers and proteins. J. Chem Phys. 143, 085101(2015).

T. Firman and Ghosh, K. Sequence charge decoration dictates coil-globule transition in intrinsically disordered proteins. J. Chem Phys. 148, 123305 (2018).

(3) Protein expression-enhancing (PEE) - just say expression-enhancing, there is no need for an acronym here.

Thank you. Since we have shown that addition of Q-rich motifs to LacZ affects protein expression rather than transcription, we think it is better to use the “PEE” acronym.

The results suggest autonomous protein expression-enhancing activities of regions of multiple proteins containing Q-rich and SCD motifs. Their definition of expression-enhancing activities is vague and the evidence they provide to support the claim is weak. While their previous work may support their claim with more evidence, it should be explained in more detail. The assay they choose is a fusion reporter measuring beta-galactosidase activity and tracking expression levels. Given the presented data they have shown that they can drive the expression of their reporters and that beta gal remains active, in addition to the increase in expression of fusion reporter during the stress response. They have not detailed what their control and mock treatment is, which makes complete understanding of their experimental approach difficult. Furthermore, their nuclear localization signal on the tag could be influencing the degradation kinetics or sequestering the reporter, leading to its accumulation and the appearance of enhanced expression. Their evidence refuting ubiquitin-mediated degradation does not have a convincing control.

Based on the experimental results, the authors then go on to perform bioinformatic analysis of SCD proteins and polyX proteins. Unfortunately, there is no clear hypothesis for what is being tested; there is a vague sense of investigating polyX/SCD regions, but I did not find the connection between the first and section compelling (especially given polar-rich regions have been shown to engage in many different functions). As such, this bioinformatic analysis largely presents as many lists of percentages without any meaningful interpretation. The bioinformatics analysis lacks any kind of rigorous statistical tests, making it difficult to evaluate the conclusions drawn. The methods section is severely lacking. Specifically, many of the methods require the reader to read many other papers. While referencing prior work is of course, important, the authors should ensure the methods in this paper provide the details needed to allow a reader to evaluate the work being presented. As it stands, this is not the case.

Thank you. As described in detail below, we have now performed rigorous statistical testing using the GofuncR package.

Overall, my major concern with this work is that the authors make two central claims in this paper (as per the Discussion). The authors claim that Q-rich motifs enhance protein expression. The implication here is that Q-rich motif IDRs are special, but this is not tested. As such, they cannot exclude the competing hypothesis ("N-terminal disordered regions enhance expression").

In fact, “N-terminal disordered regions enhance expression” exactly summarizes our hypothesis.

On pages 12-13 and Figure 4 of our preprint manuscript, we explained our hypothesis in the paragraph entitled “The relationship between PEE function, amino acid contents, and structural flexibility”.

The authors also do not explore the possibility that this effect is in part/entirely driven by mRNA-level effects (see Verma Na Comms 2019).

As pointed out by the first reviewer, we show evidence that the increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance (Figure 2), and that this phenomenon is not affected by translational quality control mutants (Figure 3).

As such, while these observations are interesting, they feel preliminary and, in my opinion, cannot be used to draw hard conclusions on how N-terminal IDR sequence features influence protein expression. This does not mean the authors are necessarily wrong, but from the data presented here, I do not believe strong conclusions can be drawn. That re-assignment of stop codons to Q increases proteome-wide Q usage. I was unable to understand what result led the authors to this conclusion.

My reading of the results is that a subset of ciliates has re-assigned UAA and UAG from the stop codon to Q. Those ciliates have more polyQ-containing proteins. However, they also have more polyN-containing proteins and proteins enriched in S/T-Q clusters. Surely if this were a stop-codon-dependent effect, we'd ONLY see an enhancement in Q-richness, not a corresponding enhancement in all polar-rich IDR frequencies? It seems the better working hypothesis is that free-floating climate proteomes are enriched in polar amino acids compared to sessile ciliates.

Thank you. These comments are not supported by the results in Figure 1.

Regardless, the absence of any kind of statistical analysis makes it hard to draw strong conclusions here.

We apologize for not explaining more clearly the results of Tables 5-7 in our preprint manuscript.

To address the concerns about our GO enrichment analysis by both reviewers, we have now performed rigorous statistical testing for SCD and polyQ protein overrepresentation using the GOfuncR package (https://bioconductor.org/packages/release/bioc/html/GOfuncR.html). GOfuncR is an R package program that conducts standard candidate vs. background enrichment analysis by means of the hypergeometric test. We then adjusted the raw p-values according to the Family-wise error rate (FWER). The same method had been applied to GO enrichment analysis of human genomes (Huttenhower, C., et al. 2009).

Curtis Huttenhower, C., Haley, E. M., Hibbs, M., A., Dumeaux, V., Barrett, D. R., Hilary A. Coller, H. A., and Olga G. Troyanskaya, O., G. Exploring the human genome with functional maps, Genome Research 19, 1093-1106 (2009).

The results presented in Author response image 5 and Author response image 6 support our hypothesis that Q-rich motifs prevail in proteins involved in specialized biological processes, including Saccharomyces cerevisiae RNA-mediated transposition, Candida albicans filamentous growth, peptidyl-glutamic acid modification in ciliates with reassigned stop codons (TAAQ and TAGQ), Tetrahymena thermophila xylan catabolism, Dictyostelium discoideum sexual reproduction, Plasmodium falciparum infection, as well as the nervous systems of Drosophila melanogaster, Mus musculus, and Homo sapiens (74). In contrast, peptidyl-glutamic acid modification and microtubule-based movement are not overrepresented with Q-rich proteins in Stentor coeruleus, a ciliate with standard stop codons.

1. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

Author response image 5.

Selection of biological processes with overrepresented SCD-containing proteins in different eukaryotes. The percentages and number of SCD-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stop codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 6.

Selection of biological processes with overrepresented polyQ-containing proteins in different eukaryotes. The percentages and numbers of polyQ-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stops codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author Response

Reviewer #1 (Public Review):

Wang and all present an interesting body of work focused on the effects of high altitude and hypoxia on erythropoiesis, resulting in erythrocytosis. This work is specifically focused on the spleen, identifying splenic macrophages as central cells in this effect. This is logical since these cells are involved in erythrophagocytosis and iron recycling. The results suggest that hypoxia induces splenomegaly with decreased number of splenic macrophages. There is also evidence that ferroptosis is induced in these macrophages, leading to cell destruction. Finally, the data suggest that ferroptosis in splenic red pulp macrophages causes the decrease in RBC clearance, resulting in erythrocytosis aka lengthening the RBC lifespan. However, there are many issues with the presented results, with somewhat superficial data, meaning the conclusions are overstated and there is decreased confidence that the hypotheses and observed results are directly causally related to hypoxia.

Major points:

1) The spleen is a relatively poorly understood organ but what is known about its role in erythropoiesis especially in mice is that it functions both to clear as well as to generate RBCs. The later process is termed extramedullary hematopoiesis and can occur in other bones beyond the pelvis, liver, and spleen. In mice, the spleen is the main organ of extramedullary erythropoiesis. The finding of transiently decreased spleen size prior to splenomegaly under hypoxic conditions is interesting but not well developed in the manuscript. This is a shortcoming as this is an opportunity to evaluate the immediate effect of hypoxia separately from its more chronic effect. Based just on spleen size, no conclusions can be drawn about what happens in the spleen in response to hypoxia.

Thank you for your insightful comments and questions. The spleen is instrumental in both immune response and the clearance of erythrocytes, as well as serving as a significant reservoir of blood in the body. This organ, characterized by its high perfusion rate and pliability, constricts under conditions of intense stress, such as during peak physical exertion, the diving reflex, or protracted periods of apnea. This contraction can trigger an immediate release of red blood cells (RBCs) into the bloodstream in instances of substantial blood loss or significant reduction of RBCs. Moreover, elevated oxygen consumption rates in certain animal species can be partially attributed to splenic contractions, which augment hematocrit levels and the overall volume of circulating blood, thereby enhancing venous return and oxygen delivery (Dane et al. J Appl Physiol, 2006, 101:289-97; Longhurst et al. Am J Physiol, 1986, 251: H502-9). In our investigation, we noted a significant contraction of the spleen following exposure to hypoxia for a period of one day. We hypothesized that the body, under such conditions, is incapable of generating sufficient RBCs promptly enough to facilitate enhanced oxygen delivery. Consequently, the spleen reacts by releasing its stored RBCs through splenic constriction, leading to a measurable reduction in spleen size.

However, we agree with you that further investigation is required to fully understand the implications of these changes. Considering the comments, we propose to extend our research by incorporating more detailed examinations of spleen morphology and function during hypoxia, including the potential impact on extramedullary hematopoiesis. We anticipate that such an expanded analysis would not only help elucidate the initial response to hypoxia but also provide insights into the more chronic effects of this condition on spleen function and erythropoiesis.

2) Monocyte repopulation of tissue resident macrophages is a minor component of the process being described and it is surprising that monocytes in the bone marrow and spleen are also decreased. Can the authors conjecture why this is happening? Typically, the expectation would be that a decrease in tissue resident macrophages would be accompanied by an increase in monocyte migration into the organ in a compensatory manner.

We appreciate your insightful query regarding the observed decrease in monocytes in the bone marrow and spleen, particularly considering the typical compensatory increase in monocyte migration into organs following a decrease in tissue resident macrophages.

The observed decrease in monocytes within the bone marrow is likely attributable to the fact that monocytes and precursor cells for red blood cells (RBCs) both originate from the same hematopoietic stem cells within the bone marrow. It is well established that exposure to hypobaric hypoxia (HH) induces erythroid differentiation specifically within the bone marrow, originating from these hematopoietic stem cells. As such, we postulate that the differentiation into monocytes is reduced under hypoxic conditions, which may subsequently cause a decrease in migration to the spleen.

Furthermore, we hypothesize that an increased migration of monocytes to other tissues under HH exposure may also contribute to the decreased migration to the spleen. The liver, which partially contributes to the clearance of RBCs, may play a role in this process. Our investigations to date have indeed identified an increased monocyte migration to the liver. We were pleased to discover an elevation in CSF1 expression in the liver following HH exposure for both 7 and 14 days. This finding was corroborated through flow cytometry, which confirmed an increase in monocyte migration to the liver.

Consequently, we propose that under HH conditions, the liver requires an increased influx of monocytes, which in turn leads to a decrease in monocyte migration to the spleen. However, it is important to note that these findings will be discussed more comprehensively in our forthcoming publication, and as such, the data pertaining to these results have not been included in the current manuscript.

3) Figure 3 does not definitively provide evidence that cell death is specifically occurring in splenic macrophages and the fraction of Cd11b+ cells is not changed in NN vs HH. Furthermore, the IHC of F4/80 in Fig 3U is not definitive as cells can express F4/80 more or less brightly and no negative/positive controls are shown for this panel.

We appreciate your insightful comments and critiques regarding Figure 3. We acknowledge that the figure, as presented, does not definitively demonstrate that cell death is specifically occurring in splenic macrophages. While it is challenging to definitively determine the occurrence of cell death in macrophages based solely on Figure 3D-F, our single-cell analysis provides strong evidence that such an event occurs. We initially observed cell death within the spleen under hypobaric hypoxia (HH) conditions, and to discern the precise cell type involved, we conducted single-cell analyses. Regrettably, we did not articulate this clearly in our preliminary manuscript. In the revised version, we have modified the sequence of Figure 3A-C and Figure 3D-F for better clarity. Besides, we observed a significant decrease in the fraction of F4/80hiCD11bhi macrophages under HH conditions compared to NN. To make the changes more evident in CD86 and CD206, we have transformed these scatter plots into histograms in our revised manuscript.

Considering the limitations of F4/80 as a conclusive macrophage identifier, we have concurrently presented the immunohistochemical (IHC) analyses of heme oxygenase-1 (HO-1). Functioning as a macrophage marker, particularly in cells involved in iron metabolism, HO-1 offers additional diagnostic accuracy. Observations from both F4/80 and HO-1 staining suggested a primary localization of positively stained cells within the splenic red pulp. Following exposure to hypoxia-hyperoxia (HH) conditions, a decrease was noted in the expression of both F4/80 and HO-1. This decrease implies that HH conditions contribute to a reduction in macrophage population and impede the iron metabolism process. In the revised version of our manuscript, we have enhanced the clarity of Figure 3U to illustrate the presence of positive staining, with an emphasis on HO-1 staining, which is predominantly observed in the red pulp.

4) The phagocytic function of splenic red pulp macrophages relative to infection cannot be used directly to understand erythrophagocytosis. The standard approach is to use opsonized RBCs in vitro. Furthermore, RBC survival is a standard method to assess erythrophagocytosis function. In this method, biotin is injected via tail vein directly and small blood samples are collected to measure the clearance of biotinilation by flow; kits are available to accomplish this. Because the method is standard, Fig 4D is not necessary and Fig 4E needs to be performed only in blood by sampling mice repeatedly and comparing the rate of biotin decline in HH with NN (not comparing 7 d with 14 d).

We appreciate your insightful comments and suggestions. We concur that the phagocytic function of splenic red pulp macrophages in the context of infection may not be directly translatable to understanding erythrophagocytosis. Given our assessment that the use of cy5.5-labeled E.coli alone may not be sufficient to accurately evaluate the phagocytic function of macrophages, we extended our study to include the use of NHS-biotin-labeled RBCs to assess phagocytic capabilities. While the presence of biotin-labeled RBCs in the blood could provide an indication of RBC clearance, this measure does not exclusively reflect the spleen's role in the process, as it fails to account for the clearance activities of other organs.

Consequently, we propose that the remaining biotin-labeled RBCs in the spleen may provide a more direct representation of the organ's function in RBC clearance and sequestration. Our observations of diminished erythrophagocytosis at both 7 and 14 days following exposure to HH guided our subsequent efforts to quantify biotin-labeled RBCs in both the circulatory system and spleen. These measurements were conducted during the 7 to 14-day span following the confirmation of impaired erythrophagocytosis. Comparative evaluation of RBC clearance rates under NN and HH conditions provided further evidence supporting our preliminary observations, with the data revealing a decrease in the RBC clearance rate in the context of HH conditions. In response to feedback from other reviewers, we have elected to exclude the phagocytic results and the diagram of the erythrocyte labeling assay. These amendments will be incorporated into the revised manuscript. The reviewers' constructive feedback has played a crucial role in refining the methodological precision and coherence of our investigation.

5) It is unclear whether Tuftsin has a specific effect on phagocytosis of RBCs without other potential confounding effects. Furthermore, quantifying iron in red pulp splenic macrophages requires alternative readily available more quantitative methods (e.g. sorted red pulp macrophages non-heme iron concentration).

We appreciate your comments and questions regarding the potential effect of Tuftsin on the phagocytosis of RBCs and the quantification of iron in red pulp splenic macrophages. Regarding the role of Tuftsin, we concur that the literature directly associating Tuftsin with erythrophagocytosis is scant. The work of Gino Roberto Corazza et al. does suggest a link between Tuftsin and general phagocytic capacity, but it does not specifically address erythrophagocytosis (Am J Gastroenterol, 1999;94:391-397). We agree that further investigations are required to elucidate the potential confounding effects and to ascertain whether Tuftsin has a specific impact on the phagocytosis of RBCs. Concerning the quantification of iron in red pulp splenic macrophages, we acknowledge your suggestion to employ readily available and more quantitative methods. We have incorporated additional Fe2+ staining in the spleen at two time points: 7 and 14 days subsequent to HH exposure (refer to the following Figure). The resultant data reveal an escalated deposition of Fe2+ within the red pulp, as evidenced in Figures 5 (panels L and M) and Figure 7 (panels L and M).

6) In Fig 5, PBMCs are not thought to represent splenic macrophages and although of some interest, does not contribute significantly to the conclusions regarding splenic macrophages at the heart of the current work. The data is also in the wrong direction, namely providing evidence that PBMCs are relatively iron poor which is not consistent with ferroptosis which would increase cellular iron.

We appreciate your insightful critique regarding Figure 5 and the interpretation of our data on peripheral blood mononuclear cells (PBMCs) in relation to splenic macrophages. We understand that PBMCs do not directly represent splenic macrophages, and we agree that any conclusions drawn from PBMCs must be considered with caution when discussing the behavior of splenic macrophages.

The primary rationale for incorporating PBMCs into our study was to investigate the potential correspondence between their gene expression changes and those observed in the spleen after HH exposure. This was posited as a working hypothesis for further exploration rather than a conclusive statement. The gene expression in PBMCs was congruous with changes in the spleen's gene expression, demonstrating an iron deficiency phenotype, ostensibly due to the mobilization of intracellular iron for hemoglobin synthesis. Thus, it is plausible that NCOA4 may facilitate iron mobilization through the degradation of ferritin to store iron.

It remains ambiguous whether ferroptosis was initiated in the PBMCs during our study. Ferroptosis primarily occurs as a response to an increase in Fe2+ rather than an overall increase in intracellular iron. Our preliminary proposition was that relative changes in gene expression in PBMCs could potentially mirror corresponding changes in protein expression in the spleen, thereby potentially indicating alterations in iron processing capacity post-HH exposure. However, we fully acknowledge that this is a conjecture requiring further empirical substantiation or clinical validation.

7) Tfr1 increase is typically correlated with cellular iron deficiency while ferroptosis consistent with iron loading. The direction of the changes in multiple elements relevant to iron trafficking is somewhat confusing and without additional evidence, there is little confidence that the authors have reached the correct conclusion. Furthermore, the results here are analyses of total spleen samples rather than specific cells in the spleen.

We appreciate your astute comments and agree that the observed increase in transferrin receptor (TfR) expression, typically associated with cellular iron deficiency, appears contradictory to the expected iron-loading state associated with ferroptosis. We understand that this apparent contradiction might engender some uncertainty about our conclusions.

In our investigation, we evaluated total spleen samples as opposed to distinct cell types within the spleen, a factor that could have contributed to the seemingly discordant findings. An integral element to bear in mind is the existence of immature RBCs in the spleen, particularly within the hematopoietic island where these immature RBCs cluster around nurse macrophages. These immature RBCs contain abundant TfR which was needed for iron uptake and hemoglobin synthesis. These cells, which prove challenging to eliminate via perfusion, might have played a role in the observed upregulation in TfR expression, especially in the aftermath of HH exposure. Our further research revealed that the expression of TfR in macrophages diminished following hypoxic conditions, thereby suggesting that the elevated TfR expression in tissue samples may predominantly originate from other cell types, especially immature RBCs (refer to subsequent Figure).

Reviewer #2 (Public Review):

The authors aimed at elucidating the development of high altitude polycythemia which affects mice and men staying in the hypoxic atmosphere at high altitude (hypobaric hypoxia; HH). HH causes increased erythropoietin production which stimulates the production of red blood cells. The authors hypothesize that increased production is only partially responsible for exaggerated red blood cell production, i.e. polycythemia, but that decreased erythrophagocytosis in the spleen contributes to high red blood cells counts.

The main strength of the study is the use of a mouse model exposed to HH in a hypobaric chamber. However, not all of the reported results are convincing due to some smaller effects which one may doubt to result in the overall increase in red blood cells as claimed by the authors. Moreover, direct proof for reduced erythrophagocytosis is compromised due to a strong spontaneous loss of labelled red blood cells, although effects of labelled E. coli phagocytosis are shown. Their discussion addresses some of the unexpected results, such as the reduced expression of HO-1 under hypoxia but due to the above-mentioned limitations much of the discussion remains hypothetical.

Thank you for your valuable feedback and insight. We appreciate the recognition of the strength of our study model, the exposure of mice to hypobaric hypoxia (HH) in a hypobaric animal chamber. We also understand your concerns about the smaller effects and their potential impact on the overall increase in red blood cells (RBCs), as well as the apparent reduced erythrophagocytosis due to the loss of labelled RBCs.

Erythropoiesis has been predominantly attributed to the amplified production of RBCs under conditions of HH. The focus of our research was to underscore the potential acceleration of hypoxia-associated polycythemia (HAPC) as a result of compromised erythrophagocytosis. Considering the spontaneous loss of labelled RBCs in vivo, we assessed the clearance rate of RBCs at the stages of 7 and 14 days within the HH environment, and subsequently compared this rate within the period from 7 to 14 days following the clear manifestation of erythrophagocytosis impairment at the two aforementioned points identified in our study. This approach was designed to negate the effects of spontaneous loss of labelled RBCs in both NN and HH conditions. Correspondingly, the results derived from blood and spleen analyses corroborated a decline in the RBC clearance rate under HH when juxtaposed with NN conditions.

Apart from the E. coli phagocytosis and the labeled RBCs experiment (this part of the results was removed in the revision), the injection of Tuftsin further substantiated the impairment of erythrophagocytosis in the HH spleen, as evidenced by the observed decrease in iron within the red pulp of the spleen post-perfusion. Furthermore, to validate our findings, we incorporated RBCs staining in splenic cells at 7 and 14 days of HH exposure, which provided concrete confirmation of impaired erythrophagocytosis (new Figure 4E).

As for the reduced expression of heme oxygenase-1 (HO-1) under hypoxia, we agree that this was an unexpected result, and we are in the process of further exploring the underlying mechanisms. It is possible that there are other regulatory pathways at play that are yet to be identified. However, we believe that by offering possible interpretations of our data and potential directions for future research, we contribute to the ongoing scientific discourse in this area.

Reviewer #3 (Public Review):

The manuscript by Yang et al. investigated in mice how hypobaric hypoxia can modify the RBC clearance function of the spleen, a concept that is of interest. Via interpretation of their data, the authors proposed a model that hypoxia causes an increase in cellular iron levels, possibly in RPMs, leading to ferroptosis, and downregulates their erythrophagocytic capacity. However, most of the data is generated on total splenocytes/total spleen, and the conclusions are not always supported by the presented data. The model of the authors could be questioned by the paper by Youssef et al. (which the authors cite, but in an unclear context) that the ferroptosis in RPMs could be mediated by augmented erythrophagocytosis. As such, the loss of RPMs in vivo which is indeed clear in the histological section shown (and is a strong and interesting finding) can be not directly caused by hypoxia, but by enhanced RBC clearance. Such a possibility should be taken into account.

Thank you for your insightful comments and constructive feedback. In their research, Youssef et al. (2018) discerned that elevated erythrophagocytosis of stressed red blood cells (RBCs) instigates ferroptosis in red pulp macrophages (RPMs) within the spleen, as evidenced in a mouse model of transfusion. This augmentation of erythrophagocytosis was conspicuous five hours post-injection of RBCs. Conversely, our study elucidated the decrease in erythrophagocytosis in the spleen after both 7 and 14 days.

Typically, macrophages exhibit an enhanced phagocytic capacity in the immediate aftermath of stress or stimulation. Nonetheless, the temporal points of observation in our study were considerably extended (seven and fourteen days). It remains uncertain whether phagocytic capability was amplified during the acute phase of HH exposure—particularly within the first day, considering that splenoconstriction under HH for one day results in the release of stored RBCs into the bloodstream—and whether this initial response could precipitate ferroptosis and subsequently diminished erythrophagocytosis at the 7 or 14 day marks under continued HH conditions.

Major points:

1) The authors present data from total splenocytes and then relate the obtained data to RPMs, which are quantitatively a minor population in the spleen. Eg, labile iron is increased in the splenocytes upon HH, but the manuscript does not show that this occurs in the red pulp or RPMs. They also measure gene/protein expression changes in the total spleen and connect them to changes in macrophages, as indicated in the model Figure (Fig. 7). HO-1 and levels of Ferritin (L and H) can be attributed to the drop in RPMs in the spleen. Are any of these changes preserved cell-intrinsically in cultured macrophages? This should be shown to support the model (relates also to lines 487-88, where the authors again speculate that hypoxia decreases HO-1 which was not demonstrated). In the current stage, for example, we do not know if the labile iron increase in cultured cells and in the spleen in vivo upon hypoxia is the same phenomenon, and why labile iron is increased. To improve the manuscript, the authors should study specifically RPMs.

We express our gratitude for your perceptive remarks. In our initial manuscript, we did not evaluate labile iron within the red pulp and red pulp macrophages (RPMs). To address this oversight, we utilized the Lillie staining method, in accordance with the protocol outlined by Liu et al., (Chemosphere, 2021, 264(Pt 1):128413), to discern Fe2+ presence within these regions. The outcomes were consistent with our antecedent Western blot and flow cytometry findings in the spleen, corroborating an increment in labile iron specifically within the red pulp of the spleen.

However, we acknowledge the necessity for other supplementary experimental efforts to further validate these findings. Additionally, we scrutinized the expression of heme oxygenase-1 (HO-1) and iron-related proteins, including transferrin receptor (TfR), ferroportin (Fpn), ferritin (Ft), and nuclear receptor coactivator 4 (NCOA4) in primary macrophages subjected to 1% hypoxic conditions, both with and without hemoglobin treatment. Our results indicated that the expression of ferroptosis-related proteins was consistent with in vivo studies, however the expression of iron related proteins was not similar in vitro and in vivo. It suggesting that the increase in labile iron in cultured cells and the spleen in vivo upon hypoxia are not identical phenomena. However, the precise mechanism remains elusive.

In our study, we observed a decrease in HO-1 protein expression following 7 and 14 days of HH exposure, as shown in Figure 3U, 5A, and S1A. This finding contradicts previous research that identified HO-1 as a hypoxia-inducible factor (HIF) target under hypoxic conditions (P J Lee et al., 1997). Our discussion, therefore, addressed the potential discrepancy in HO-1 expression under HH. According to our findings, HO-1 regulation under HH appears to be predominantly influenced by macrophage numbers and the RBCs to be processed in the spleen or macrophages, rather than by hypoxia alone.

It is challenging to discern whether the increased labile iron observed in vitro accurately reflects the in vivo phenomenon, as replicating the iron requirements for RBCs production induced by HH in vitro is inherently difficult. However, by integrating our in vivo and in vitro studies, we determined that the elevated Fe2+ levels were not dependent on HO-1 protein expression, as HO-1 levels was increased in vitro while decreasing in vivo under hypoxic/HH exposure.

2) The paper uses flow cytometry, but how this method was applied is suboptimal: there are no gating strategies, no indication if single events were determined, and how cell viability was assessed, which are the parent populations when % of cells is shown on the graphs. How RBCs in the spleen could be analyzed without dedicated cell surface markers? A drop in splenic RPMs is presented as the key finding of the manuscript but Fig. 3M shows gating (suboptimal) for monocytes, not RPMs. RPMs are typically F4/80-high, CD11-low (again no gating strategy is shown for RPMs). Also, the authors used single-cell RNAseq to detect a drop in splenic macrophages upon HH, but they do not indicate in Fig. A-C which cluster of cells relates to macrophages. Cell clusters are not identified in these panels, hence the data is not interpretable).

Thank you for your comments and constructive critique regarding our flow cytometry methodology and presentation. We understand the need for greater transparency and detailed explanation of our procedures, and we acknowledge that the lack of gating strategies and other pertinent information in our initial manuscript may have affected the clarity of our findings.

In our initial report, we provided an overview of the decline in migrated macrophages (F4/80hiCD11bhi), including both M1 and M2 expression in migrated macrophages, as illustrated in Figure 3, but did not specifically address the changes in red pulp macrophages (RPMs). Based on previous results, it is difficult to identify CD11b- and CD11blo cells. We will repeat the results and attempt to identify F4/80hiCD11blo cells in the revised manuscript. The results of the reanalysis are now included (Figure 3M). However, single-cell in vivo analysis studies may more accurately identify specific cell types that decrease after exposure to HH.

Furthermore, we substantiated the reduction in red pulp, as evidenced by Figure 4J, given that iron processing primarily occurs within the red pulp. In Figure 3, our initial objective was merely to illustrate the reduction in total macrophages in the spleen following HH exposure.

To further clarify the characterization of various cell types, we conducted a single-cell analysis. Our findings indicated that clusters 0,1,3,4,14,18, and 29 represented B cells, clusters 2, 10, 12, and 28 represented T cells, clusters 15 and 22 corresponded to NK cells, clusters 5, 11, 13, and 19 represented NKT cells, clusters 6, 9, and 24 represented cell cycle cells, clusters 26 and 17 represented plasma cells, clusters 21 and 23 represented neutrophils, cluster 30 represented erythrocytes, and clusters 7, 8, 16, 20, 24, and 27 represented dendritic cells (DCs) and macrophages, as depicted in Figure 3E.

3) The authors draw conclusions that are not supported by the data, some examples: a) they cannot exclude eg the compensatory involvement of the liver in the RBCs clearance (the differences between HH sham and HH splenectomy is mild in Fig. 2 E, F and G).

Thank you for your insightful comments and for pointing out the potential involvement of other organs, such as the liver, in the RBC clearance under HH conditions. We concur with your observation that the differences between the HH sham and HH splenectomy conditions in Fig. 2 E, F, and G are modest. This could indeed suggest a compensatory role of other organs in RBC clearance when splenectomy is performed. Our intent, however, was to underscore the primary role of the spleen in this process under HH exposure.

In fact, after our initial investigations, we conducted a more extensive study examining the role of the liver in RBC clearance under HH conditions. Our findings, as illustrated in the figures submitted with this response, indeed support a compensatory role for the liver. Specifically, we observed an increase in macrophage numbers and phagocytic activity in the liver under HH conditions. Although the differences in RBC count between the HH sham and HH splenectomy conditions may seem minor, it is essential to consider the unit of this measurement, which is value*1012/ml. Even a small numerical difference can represent a significant biological variation at this scale.

b) splenomegaly is typically caused by increased extramedullary erythropoiesis, not RBC retention. Why do the authors support the second possibility? Related to this, why do the authors conclude that data in Fig. 4 G,H support the model of RBC retention? A significant drop in splenic RBCs (poorly gated) was observed at 7 days, between NN and HH groups, which could actually indicate increased RBC clearance capacity = less retention.

Prior investigations have predominantly suggested that spleen enlargement under hypoxic conditions stems from the spleen's extramedullary hematopoiesis. Nevertheless, an intriguing study conducted in 1994 by the General Hospital of Xizang Military Region reported substantial exaggeration and congestion of splenic sinuses in high altitude polycythemia (HAPC) patients. This finding was based on the dissection of spleens from 12 patients with HAPC (Zou Xunda, et al., Southwest Defense Medicine, 1994;5:294-296). Moreover, a recent study indicated that extramedullary erythropoiesis reaches its zenith between 3 to 7 days (Wang H et al., 2021).

Considering these findings, the present study postulates that hypoxia-induced inhibition of erythrophagocytosis may lead to RBC retention. However, we acknowledge that the manuscript in its current preprint form does not offer conclusive evidence to substantiate this hypothesis. To bridge this gap, we further conducted experiments where the spleen was perfused, and total cells were collected post HH exposure. These cells were then smeared onto slides and subjected to Wright staining. Our results unequivocally demonstrate an evident increase in deformation and retention of RBCs in the spleen following 7 and 14 days of HH exposure. This finding strengthens our initial hypothesis and contributes a novel perspective to the understanding of splenic responses under hypoxic conditions.

c) lines 452-54: there is no data for decreased phagocytosis in vivo, especially in the context of erythrophagocytosis. This should be done with stressed RBCs transfusion assays, very good examples, like from Youssef et al. or Threul et al. are available in the literature.

Thanks. In their seminal work, Youssef and colleagues demonstrated that the transfusion of stressed RBCs triggers erythrophagocytosis and subsequently incites ferroptosis in red pulp macrophages (RPMs) within a span of five hours. Given these observations, the applicability of this model to evaluate macrophage phagocytosis in the spleen or RPMs under HH conditions may be limited, as HH has already induced erythropoiesis in vivo. In addition, it was unclear whether the membrane characteristics of stress induced RBCs were similar to those of HH induced RBCs, as this is an important signal for in vivo phagocytosis. The ambiguity arises from the fact that we currently lack sufficient knowledge to discern whether the changes in phagocytosis are instigated by the presence of stressed RBCs or by changes of macrophages induced by HH in vivo. Nonetheless, we appreciate the potential value of this approach and intend to explore its utility in our future investigations. The prospect of distinguishing the effects of stressed RBCs from those of HH on macrophage phagocytosis is an intriguing line of inquiry that could yield significant insights into the mechanisms governing these physiological processes. We will investigate this issue in our further study.

d) Line 475 - ferritinophagy was not shown in response to hypoxia by the manuscript, especially that NCOA4 is decreased, at least in the total spleen.

Drawing on the research published in eLife in 2015, it was unequivocally established that ferritinophagy, facilitated by Nuclear Receptor Coactivator 4 (NCOA4), is indispensable for erythropoiesis. This process is modulated by iron-dependent HECT and RLD domain containing E3 ubiquitin protein ligase 2 (HERC2)-mediated proteolysis (Joseph D Mancias et al., eLife. 2015; 4: e10308). As is widely recognized, NCOA4 plays a critical role in directing ferritin (Ft) to the lysosome, where both NCOA4 and Ft undergo coordinated degradation.

In our study, we provide evidence that exposure to HH stimulates erythropoiesis (Figure 1). We propose that this, in turn, could promote ferritinophagy via NCOA4, resulting in a decrease in NCOA4 protein levels post-HH exposure. We will further increase experiments to verify this concern. This finding not only aligns with the established understanding of ferritinophagy and erythropoiesis but also adds a novel dimension to the understanding of cellular responses to hypoxic conditions.

4) In a few cases, the authors show only representative dot plots or histograms, without quantification for n>1. In Fig. 4B the authors write about a significant decrease (although with n=1 no statistics could be applied here; of note, it is not clear what kind of samples were analyzed here). Another example is Fig. 6I. In this case, it is even more important as the data are conflicting the cited article and the new one: PMCID: PMC9908853 which shows that hypoxia stimulates efferocytosis. Sometimes the manuscript claim that some changes are observed, although they are not visible in representative figures (eg for M1 and M2 macrophages in Fig. 3M)

We recognize that our initial portrayal of Figure 4B was lacking in precision, given that it did not include the corresponding statistical graph. While our results demonstrated a significant reduction in the ability to phagocytose E. coli, in line with the recommendations of other reviewers, we have opted to remove the results pertaining to E. coli phagocytosis in this revision, as they primarily reflected immune function. In relation to PMC9908853, which reported metabolic adaptation facilitating enhanced macrophage efferocytosis in limited-oxygen environments, it is worth noting that the macrophages investigated in this study were derived from ER-Hoxb8 macrophage progenitors following the removal of β-estradiol. Consequently, questions arise regarding the comparability between these cultured macrophages and primary macrophages obtained fresh from the spleen post HH exposure. The characteristics and functions of these two different macrophage sources may not align precisely, and this distinction necessitates further investigation.

5) There are several unclear issues in methodology:

• what is the purity of primary RPMs in the culture? RPMs are quantitatively poorly represented in splenocyte single-cell suspensions. This reviewer is quite skeptical that the processing of splenocytes from approx 1 mm3 of tissue was sufficient to establish primary RPM cultures. The authors should prove that the cultured cells were indeed RPMs, not monocyte-derived macrophages or other splenic macrophage subtypes.

Thank you for your thoughtful comments and inquiries. Firstly, I apologize if we did not make it clear in the original manuscript. The purity of the primary RPMs in our culture was found to be approximately 40%, as identified by F4/80hiCD11blo markers using flow cytometry. We recognize that RPMs are typically underrepresented in splenocyte single-cell suspensions, and the concern you raise about the potential for contamination by other cell types is valid.

We apologize for any ambiguities in the methodological description that may have led to misunderstandings during the review. Indeed, the entirety of the spleen is typically employed for splenic macrophage culture. The size of the spleen can vary dependent on the species and age of the animal, but in mice, it is commonly approximately 1 cm in length. The spleen is then dissected into minuscule fragments, each approximately 1 mm3 in volume, to aid in enzymatic digestion. This procedure does not merely utilize a single 1 mm3 tissue fragment for RPMs cultures. Although the isolation and culture of spleen macrophages can present considerable challenges, our method has been optimized to enhance the yield of this specific cell population.

• (around line 183) In the description of flow cytometry, there are several missing issues. In 1) it is unclear which type of samples were analyzed. In 2) it is not clear how splenocyte cell suspension was prepared.

1) Whole blood was extracted from the mice and collected into an anticoagulant tube, which was then set aside for subsequent thiazole orange (TO) staining. 2) Splenic tissue was procured from the mice and subsequently processed into a single-cell suspension using a 40 μm filter. The erythrocytes within the entire sample were subsequently lysed and eliminated, and the remaining cell suspension was resuspended in phosphate-buffered saline (PBS) in preparation for ensuing analyses.

We have meticulously revised these methodological details in the corresponding section of the manuscript to ensure clarity and precision.

• In line 192: what does it mean: 'This step can be omitted from cell samples'?

The methodology employed for the quantification of intracellular divalent iron content and lipid peroxidation level was executed as follows: Splenic tissue was first processed into a single cell suspension, subsequently followed by the lysis of RBCs. It should be noted that this particular stage is superfluous when dealing with isolated cell samples. Subsequently, a total of 1 × 106 cells were incubated with 100 μL of BioTracker Far-red Labile Fe2+ Dye (1 mM, Sigma, SCT037, USA) for a duration of 1 hour, or alternatively, C11-Bodipy 581/591 (10 μM, Thermo Fisher, D3861, USA) for a span of 30 minutes. Post incubation, cells were thoroughly washed twice with PBS. Flow cytometric analysis was subsequently performed, utilizing the FL6 (638 nm/660 nm) channel for the determination of intracellular divalent iron content, and the FL1 (488 nm/525 nm) channel for the quantification of the lipid peroxidation level.

• 'TO method' is not commonly used anymore and hence it was unclear to this Reviewer. Reticulocytes should be analyzed with proper gating, using cell surface markers.

We are appreciative of your astute observation pertaining to the methodology we employed to analyze reticulocytes in our study. We value your recommendation to utilize cell surface markers for effective gating, which indeed represents a more modern and accurate approach. However, as reticulocyte identification is not the central focus of our investigation, we opted for the TO staining method—due to its simplicity and credibility of results. In our initial exploration, we adopted the TO staining method in accordance with the protocol outlined (Sci Rep, 2018, 8(1):12793), primarily owing to its established use and demonstrated efficacy in reticulocyte identification.

• The description of 'phagocytosis of E. coli and RBCs' in the Methods section is unclear and incomplete. The Results section suggests that for the biotinylated RBCs, phagocytosis? or retention? Of RBCs was quantified in vivo, upon transfusion. However, the Methods section suggests either in vitro/ex vivo approach. It is vague what was indeed performed and how in detail. If RBC transfusion was done, this should be properly described. Of note, biotinylation of RBCs is typically done in vivo only, being a first step in RBC lifespan assay. The such assay is missing in the manuscript. Also, it is not clear if the detection of biotinylated RBCs was performed in permeablized cells (this would be required).

Thanks for the comments. In our initial methodology, we employed Cy5.5-labeled Escherichia coli to probe phagocytic function, albeit with the understanding that this may not constitute the most ideal model for phagocytosis detection within this context (in light of recommendations from other reviewers, we have removed the E. coli phagocytosis results from this revision, as they predominantly mirror immune function). Our fundamental aim was to ascertain whether HH compromises the erythrophagocytic potential of splenic macrophages. In pursuit of this, we subsequently analyzed the clearance of biotinylated RBCs in both the bloodstream and spleen to assess phagocytic functionality in vivo.

In the present study, instead of transfusing biotinylated RBCs into mice, we opted to inject N-Hydroxysuccinimide (NHS)-biotin into the bloodstream. NHS-biotin is capable of binding with cell membranes in vivo and can be recognized by streptavidin-fluorescein isothiocyanate (FITC) after cells are extracted from the blood or spleen in vitro. Consequently, biotin-labeled RBCs were detectable in both the blood and spleen following NHS-biotin injection for a duration of 21 days.

Ultimately, we employed flow cytometry to analyze the NHS-biotin labeled RBCs in the blood or spleen. This method facilitates the detection of live cells and is not applicable to permeabilized cells. We believe this approach better aligns with our investigative goals and offers a more robust evaluation of erythrophagocytic function under hypoxic conditions.

Author response:

Reviewer #1 (Public review):

Summary:

Jocher, Janssen, et al examine the robustness of comparative functional genomics studies in primates that make use of induced pluripotent stem cell-derived cells. Comparative studies in primates, especially amongst the great apes, are generally hindered by the very limited availability of samples, and iPSCs, which can be maintained in the laboratory indefinitely and defined into other cell types, have emerged as promising model systems because they allow the generation of data from tissues and cells that would otherwise be unobservable.

Undirected differentiation of iPSCs into many cell types at once, using a method known as embryoid body differentiation, requires researchers to manually assign all cell types in the dataset so they can be correctly analysed. Typically, this is done using marker genes associated with a specific cell type. These are defined a priori, and have historically tended to be characterised in mice and humans and then employed to annotate other species. Jocher, Janssen, et al ask if the marker genes and features used to define a given cell type in one species are suitable for use in a second species, and then quantify the degree of usefulness of these markers. They find that genes that are informative and cell type specific in a given species are less valuable for cell type identification in other species, and that this value, or transferability, drops off as the evolutionary distance between species increases.

This paper will help guide future comparative studies of gene expression in primates (and more broadly) as well as add to the growing literature on the broader challenges of selecting powerful and reliable marker genes for use in single-cell transcriptomics.

Strengths:

Marker gene selection and cell type annotation is a challenging problem in scRNA studies, and successful classification of cells often requires manual expert input. This can be hard to reproduce across studies, as, despite general agreement on the identity of many cell types, different methods for identifying marker genes will return different sets of genes. The rise of comparative functional genomics complicates this even further, as a robust marker gene in one species need not always be as useful in a different taxon. The finding that so many marker genes have poor transferability is striking, and by interrogating the assumption of transferability in a thorough and systematic fashion, this paper reminds us of the importance of systematically validating analytical choices. The focus on identifying how transferability varies across different types of marker genes (especially when comparing TFs to lncRNAs), and on exploring different methods to identify marker genes, also suggests additional criteria by which future researchers could select robust marker genes in their own data.

The paper is built on a substantial amount of clearly reported and thoroughly considered data, including EBs and cells from four different primate species - humans, orangutans, and two macaque species. The authors go to great lengths to ensure the EBs are as comparable as possible across species, and take similar care with their computational analyses, always erring on the side of drawing conservative conclusions that are robustly supported by their data over more tenuously supported ones that could be impacted by data processing artefacts such as differences in mappability, etc. For example, I like the approach of using liftoff to robustly identify genes in non-human species that can be mapped to and compared across species confidently, rather than relying on the likely incomplete annotation of the non-human primate genomes. The authors also provide an interactive data visualisation website that allows users to explore the dataset in depth, examine expression patterns of their own favourite marker genes and perform the same kinds of analyses on their own data if desired, facilitating consistency between comparative primate studies.

We thank the Reviewer for their kind assessment of our work.

Weaknesses and recommendations:

(1) Embryoid body generation is known to be highly variable from one replicate to the next for both technical and biological reasons, and the authors do their best to account for this, both by their testing of different ways of generating EBs, and by including multiple technical replicates/clones per species. However, there is still some variability that could be worth exploring in more depth. For example, the orangutan seems to have differentiated preferentially towards cardiac mesoderm whereas the other species seemed to prefer ectoderm fates, as shown in Figure 2C. Likewise, Supplementary Figure 2C suggests a significant unbalance in the contributions across replicates within a species, which is not surprising given the nature of EBs, while Supplementary Figure 6 suggests that despite including three different clones from a single rhesus macaque, most of the data came from a single clone. The manuscript would be strengthened by a more thorough exploration of the intra-species patterns of variability, especially for the taxa with multiple biological replicates, and how they impact the number of cell types detected across taxa, etc.

You are absolutely correct in pointing out that the large clonal variability in cell type composition is a challenge for our analysis. We also noted the odd behavior of the orangutan EBs, and their underrepresentation of ectoderm. There are many possible sources for these variable differentiation propensities: clone, sample origin (in this case urine) and individual. However, unfortunately for the orangutan, we have only one individual and one sample origin and thus cannot say whether this germ layer preference says something about the species or is due to our specific sample.

Because of this high variability from multiple sources, getting enough cell types with an appreciable overlap between species was limiting to analyses. In order to be able to derive meaningful conclusions from intra-species analyses and the impact of different sources of variation on cell type propensity, we would need to sequence many more EBs with an experimental design that balances possible sources of variation. This would go beyond the scope of this study.

Instead, here we control for intra-species variation in our analyses as much as possible: For the analysis of cell type specificity and conservation the comparison is relative for the different specificity degrees (Figure 3C).  For the analysis of marker gene conservation, we explicitly take intra-species variation into account (Figure 4D).

The same holds for the temporal aspect of the data, which is not really discussed in depth despite being a strength of the design. Instead, days 8 and 16 are analysed jointly, without much attention being paid to the possible differences between them.

Concerning the temporal aspect, indeed we knowingly omitted to include an explicit comparison of day 8 and day 16 EBs, because we felt that it was not directly relevant to our main message. Our pseudotime analysis showed that the differences of the two time points were indeed a matter of degree and not so much of quality. All major lineages were already present at day 8 and even though day 8 cells had on average earlier pseudotimes, there was a large overlap in the pseudotime distributions between the two sampling time points (Author response image 1). That is why we decided to analyse the data together.

Are EBs at day 16 more variable between species than at day 8? Is day 8 too soon to do these kinds of analyses?

When we started the experiment, we simply did not know what to expect. We were worried that cell types at day 8 might be too transient, but longer culture can also introduce biases. That is why we wanted to look at two time points, however as mentioned above the differences are in degree.

Concerning the cell type composition: yes, day 16 EBs are more heterogeneous than day 8 EBs. Firstly, older EBs have more distinguishable cell types and hence even if all EBs had identical composition, the sampling variance would be higher given that we sampled a similar number of cells from both time points. Secondly, in order to grow EBs for a longer time, we moved them from floating to attached culture on day 8 and it is unclear how much variance is added by this extra handling step.

Are markers for earlier developmental progenitors better/more transferable than those for more derived cell types?

We did not see any differences in the marker conservation between early and late cell types, but we have too little data to say whether this carries biological meaning.

Author response image 1.

Pseudotime analysis for a differentiation trajectory towards neurons. Single cells were first aggregated into metacells per species using SEACells (Persad et al. 2023). Pluripotent and ectoderm metacells were then integrated across all four species using Harmony and a combined pseudotime was inferred with Slingshot (Street et al. 2018), specifying iPSCs as the starting cluster. Here, lineage 3 is shown, illustrating a differentiation towards neurons. (A) PHATE embedding colored by pseudotime (Moon et al. 2019). (B) PHATE embedding colored by celltype. (C) Pseudotime distribution across the sampling timepoints (day 8 and day 16) in different species.

(2) Closely tied to the point above, by necessity the authors collapse their data into seven fairly coarse cell types and then examine the performance of canonical marker genes (as well as those discovered de novo) across the species. However some of the clusters they use are somewhat broad, and so it is worth asking whether the lack of specificity exhibited by some marker genes and driving their conclusions is driven by inter-species heterogeneity within a given cluster.

Author response image 2.

UMAP visualization for the Harmony-integrated dataset across all four species for the seven shared cell types, colored by cell type identity (A) and species (B).

Good point, if we understand correctly, the concern is that in our relatively broadly defined cell types, species are not well mixed and that this in turn is partly responsible for marker gene divergence. This problem is indeed difficult to address, because most approaches to evaluate this require integration across species which might lead to questionable results (see our Discussion).

Nevertheless, we attempted an integration across all four species. To this end, we subset the cells for the 7 cell types that we found in all four species and visualized cell types and species in the UMAPs above (Author response image 2).

We see that cardiac fibroblasts appear poorly integrated in the UMAP, but they still have very transferable marker genes across species. We quantified integration quality using the cell-specific mixing score (cms) (Lütge et al. 2021) and indeed found that the proportion of well integrated cells is lowest for cardiac fibroblasts (Author response image 3A). On the other end of the cms spectrum, neural crest cells appear to have the best integration across species, but their marker transferability between species is rather worse than for cardiac fibroblasts (Supplementary Figure 9). Cell-type wise calculated rank-biased overlap scores that we use for marker gene conservation show the same trends (Author response image 3B) as the F1 scores for marker gene transferability.  Hence, given our current dataset we do not see any indication that the low marker gene conservation is a result of too broadly defined cell types.

Author response image 3.

(A) Evaluation of species mixing per cell type in the Harmony-integrated dataset, quantified by the fraction of cells with an adjusted cell-specific mixing score (cms) above 0.05. (B) Summary of rank-biased overlap (RBO) scores per cell type to assess concordance of marker gene rankings for all species pairs.

Reviewer #2 (Public review):

Summary:

The authors present an important study on identifying and comparing orthologous cell types across multiple species. This manuscript focuses on characterizing cell types in embryoid bodies (EBs) derived from induced pluripotent stem cells (iPSCs) of four primate species, humans, orangutans, cynomolgus macaques, and rhesus macaques, providing valuable insights into cross-species comparisons.

Strengths:

To achieve this, the authors developed a semi-automated computational pipeline that integrates classification and marker-based cluster annotation to identify orthologous cell types across primates. This study makes a significant contribution to the field by advancing cross-species cell type identification.

We thank the reviewer for their positive and thoughtful feedback.

Weaknesses:

However, several critical points need to be addressed.

(1) Use of Liftoff for GTF Annotation

The authors used Liftoff to generate GTF files for Pongo abelii, Macaca fascicularis, and Macaca mulatta by transferring the hg38 annotation to the corresponding primate genomes. However, it is unclear why they did not use species-specific GTF files, as all these genomes have existing annotations. Why did the authors choose not to follow this approach?

As Reviewer 1 also points out, also we have observed that the annotation of non-human primates often has truncated 3’UTRs. This is especially problematic for 3’ UMI transcriptome data as the ones in the 10x dataset that we present here. To illustrate this we compared the Liftoff annotation derived from Gencode v32,  that we also used throughout our manuscript to the Ensembl gene annotation Macaca_fascicularis_6.0.111. We used transcriptomes from human and cynomolgus iPSC bulk RNAseq  (Kliesmete et al. 2024) using the Prime-seq protocol (Janjic et al. 2022) which is very similar to 10x in that it also uses 3’ UMIs. On average using Liftoff produces higher counts than the Ensembl annotation (Author response image 4A). Moreover, when comparing across species, using Ensembl for the macaque leads to an asymmetry in differentially expressed genes, with apparently many more up-regulated genes in humans. In contrast, when we use the Liftoff annotation, we detect fewer DE-genes and a similar number of genes is up-regulated in macaques as in humans (Author response image 4B). We think that the many more DE-genes are artifacts due to mismatched annotation in human and cynomolgus macaques. We illustrate this for the case of the transcription factor SALL4 in Author response image 4 C,D.  The Ensembl annotation reports 2 transcripts, while Liftoff from Gencode v32 suggests 5 transcripts, one of which has a longer 3’UTR. This longer transcript is also supported by Nanopore data from macaque iPSCs. The truncation of the 3’UTR in this case leads to underestimation of the expression of SALL4 in macaques and hence SALL4 is detected as up-regulated in humans (DESeq2: LFC= 1.34, p-adj<2e-9). In contrast, when using the Liftoff annotation SALL4 does not appear to be DE between humans and macaques (LFC=0.33, p.adj=0.20).

Author response image 4. 

(A) UMI-counts/ gene for the same cynomolgus macaque iPSC samples. On the x-axis the gtf file from Ensembl Macaca_fascicularis_6.0.111 was used to count and on the y-axis we used our filtered Liftoff annotation that transferred the human gene models from Gencode v32. (B) The # of DE-genes between human  and cynomolgus iPSCs detected with DESeq2. In Liftoff, we counted human samples using Gencode v32 and compared it to the Liftoff annotation of the same human gene models to macFas6. In Ensembl, we use Gencode v32 for the human and  Ensembl Macaca_fascicularis_6.0.111 for the Macaque. For both comparisons we subset the genes to only contain one to one orthologues as annotated in biomart. Up and down regulation is relative to human expression. C) Read counts for one example gene SALL4. Here we used in addition to the Liftoff and Ensembl annotation also transcripts derived from Nanopore cDNA sequencing of cynomolgus iPSCs. D) Gene models for SALL4 in the space of MacFas6 and a coverage for iPSC-Prime-seq bulk RNA-sequencing.

(2) Transcript Filtering and Potential Biases

The authors excluded transcripts with partial mapping (<50%), low sequence identity (<50%), or excessive length differences (>100 bp and >2× length ratio). Such filtering may introduce biases in read alignment. Did the authors evaluate the impact of these filtering choices on alignment rates?

We excluded those transcripts from analysis in both species, because they present a convolution of sequence-annotation differences and expression. The focus in our study is on regulatory evolution and we knowingly omit marker differences that are due to a marker being mutated away, we will make this clearer in the text of a revised version.

(3) Data Integration with Harmony

The methods section does not specify the parameters used for data integration with Harmony. Including these details would clarify how cross-species integration was performed.

We want to stress  that none of our conservation and marker gene analyses relies on cross-species integration. We only used the Harmony integrated data for visualisation in Figure 1 and the rough germ-layer check up in Supplementary Figure S3.  We will add a better description in the revised version.

References

Janjic, Aleksandar, Lucas E. Wange, Johannes W. Bagnoli, Johanna Geuder, Phong Nguyen, Daniel Richter, Beate Vieth, et al. 2022. “Prime-Seq, Efficient and Powerful Bulk RNA Sequencing.” Genome Biology 23 (1): 88.

Kliesmete, Zane, Peter Orchard, Victor Yan Kin Lee, Johanna Geuder, Simon M. Krauß, Mari Ohnuki, Jessica Jocher, Beate Vieth, Wolfgang Enard, and Ines Hellmann. 2024. “Evidence for Compensatory Evolution within Pleiotropic Regulatory Elements.” Genome Research 34 (10): 1528–39.

Lütge, Almut, Joanna Zyprych-Walczak, Urszula Brykczynska Kunzmann, Helena L. Crowell, Daniela Calini, Dheeraj Malhotra, Charlotte Soneson, and Mark D. Robinson. 2021. “CellMixS: Quantifying and Visualizing Batch Effects in Single-Cell RNA-Seq Data.” Life Science Alliance 4 (6): e202001004.

Moon, Kevin R., David van Dijk, Zheng Wang, Scott Gigante, Daniel B. Burkhardt, William S. Chen, Kristina Yim, et al. 2019. “Visualizing Structure and Transitions in High-Dimensional Biological Data.” Nature Biotechnology 37 (12): 1482–92.

Persad, Sitara, Zi-Ning Choo, Christine Dien, Noor Sohail, Ignas Masilionis, Ronan Chaligné, Tal Nawy, et al. 2023. “SEACells Infers Transcriptional and Epigenomic Cellular States from Single-Cell Genomics Data.” Nature Biotechnology 41 (12): 1746–57.

Street, Kelly, Davide Risso, Russell B. Fletcher, Diya Das, John Ngai, Nir Yosef, Elizabeth Purdom, and Sandrine Dudoit. 2018. “Slingshot: Cell Lineage and Pseudotime Inference for Single-Cell Transcriptomics.” BMC Genomics 19 (1): 477.

Author response:

We thank the reviewers for their thorough evaluation and constructive feedback on our manuscript.

We think that their valuable suggestions will strengthen the manuscript and help us clarify several important points.

All reviewers acknowledged the importance of our theoretical results and network classification in making pattern formation analysis a more tractable problem. At the same time, they have also raised a number of important concerns that we shall carefully consider.

A. A major clarification that the reviewers found important concerns the definition of non-trivial pattern transformations and its generalization to higher dimensions. In this regard, the reviewers’ comments are:

Reviewer #1:

(on non-trivial pattern transformations):

(3) All modelling is confined to one spatial dimension, and the very definition of a "non-trivial" transformation is framed in terms of peak positions along a line, which clearly must be reformulated for higher dimensions. It's well-known that diffusions in 1, 2, and 3 dimensions are also dramatically different, so the relevance of the three-class taxonomy to real multicellular tissues remains unclear, or at least should be explained in more detail. Reviewer #2 (on non-trivial pattern transformations):

(5) The definition of non-trivial pattern formation is provided only in the Supplementary Information, despite its central importance for interpreting the main results. It would significantly improve clarity if this definition were included and explained in the main text. Additionally, it remains unclear how the definition is consistently applied across the different initial conditions. In particular, the authors should clarify how slope-based measures are determined for both the random noise and sharp peak/step function initial states. Furthermore, the authors do not specify how the sign function is evaluated at zero. If the standard mathematical definition sgn(0)=0 is used, then even a simple widening of a peak could fulfill the criterion for nontrivial pattern transformation.

We agree with Reviewer #2 that including a more detailed definition of non-trivial pattern transformation in the main text would enhance the clarity of the paper. The one-dimensional (1D) definition currently provided in the Supplementary Information was chosen because all computations presented therein involve exclusively one-dimensional patterns. However, we acknowledge that this definition, as it was, did not have a totally unambiguous generalization  to higher dimensions. Therefore, in a revised version of the manuscript, we will incorporate an expanded definition applicable to higher-dimensional cases.

This general definition of a non-trivial pattern transformation should make no reference to the sign of spatial derivatives of either the initial or resulting patterns. Specifically, a pattern transformation is considered non-trivial if it satisfies the following criteria:

- It is heterogeneous: The resulting pattern is heterogeneous in space.

- It is rearranging: The arrangement of critical points (i.e. peaks, valleys and saddle points in a gene product concentration) along the domain in the resulting pattern of a gene product is different to the arrangement of critical points in its initial pattern. This includes the emergence of new critical points, the disappearance of existing ones, or the spatial displacement of critical points from one location to another.

- It is non-replicating: The spatial arrangement of critical points in the pattern of one gene product must differ from that of any other upstream gene product.

Nonetheless, our two initial patterns are spatially discontinuous functions: in homogeneous initial patterns, the white noise is discontinuous by definition; and for the spike and spike+homogeneous initial patterns, we use sharp spikes defined by the rectangular function, which is discontinuous at the spike boundaries. Therefore, the aforementioned definition should be supplemented with the following two ad hoc assumptions:

- Homogeneous initial patterns do not comprise any critical point. White noise in this type of initial patterns represents small thermodynamic fluctuations around the steady state and, for the purpose of pattern transformation, this is equivalent to a constant concentration along the domain.

- Spike and spike+homogeneous initial patterns each contain a single critical point located at the center of the spike. The sharp spikes, modeled using the rectangular function, serve as a theoretical idealization to facilitate mathematical analysis. Once diffusion begins to act, these sharp boundaries are smoothed into differentiable gradients, maintaining a unique critical point at the center of the initial spike, which is the most relevant information for pattern transformation.

Finally, it is worth recalling that our gene network classification is fundamentally based on an analysis of the dispersion relation associated with the gene network, and the construction of this dispersion relation is independent of the spatial dimensionality of the domain (i.e. it does not require assuming any specific number of dimensions). The fact that the description of this dispersion relation was in the SI may have been non-ideal for the understandability of the article and will, consequently, be moved to the main text in an upcoming version of the article. Thus, the gene networks that can lead to pattern transformation are the same in 1D, 2D or 3D. As for the resulting patterns, the broad description we provide also applies to any number of dimensions; these would be periodic, non periodic as in the amplified noise patterns or non periodic as in the hierarchic networks. For the latter notice that, except for boundary effects that we later discuss, the spike initial condition is radially symmetric and thus, the patterns resulting from it will also be radially symmetric. We will make this point more explicit in a revised version of the article, especially since, as suggested, this important portion of the Supplementary Information will be incorporated into the main text.

Reviewer 2 suggests that with our definition of non-trivial pattern transformation, the simple widening of a concentration peak would constitute a non-trivial pattern transformation. This is not the case, as already shown in the figures as a example, since in a widening there is no change in the position of the critical point. A different situation applies if a wide and completely flat concentration peak (i.e. a plateau) forms. As we will explain in the coming version this is not possible because of requirement R5.

We think that this clarification of the definition of non-trivial pattern transformation will also help clarify the next point (B below) since it would make it clearer that this article does not intend to explain which specific resulting pattern would arise from any given gene network.

B. The main concern among these relates to the validity of our linearization of the model equations and the extension of the results obtained for the linear system to the fully nonlinear system. In this regard, the reviewers’ comments are:

Reviewer #1:

(on linearization):

(2) A central step in the model formulation is the linearisation of the reaction term around a homogeneous steady state; higher-order kinetics, including ubiquitous bimolecular sinks such as A + B → AB, are simply collapsed into the Jacobian without any stated amplitude bound on the perturbations. Because the manuscript never analyses how far this assumption can be relaxed, the robustness of the three-class taxonomy under realistic nonlinear reactions or large spike amplitudes remains uncertain.

Reviewer #2:

(on linearization):

(2) Most of the proofs presented in the Supplementary Information rely on linearized versions of the governing equations, and it remains unclear how these results extend to the fully nonlinear system. We are concerned that the generality of the conclusions drawn from the linear analysis may be overstated in the main text. For example, in Section S3, the authors introduce the concept of dynamic equivalence of transitive chains (Proposition S3.1) and intracellular transitive M-branching (Proposition S3.2), which pertains to the system's steady-state behavior. However, the proof is based solely on the linearized equations, without additional justification for why the result should hold in the presence of nonlinearities. Moreover, the linearized system is used to analyze the response to a "spike initial pattern of arbitrary height C" (SI Chapter S5.1), yet it is not clear how conclusions derived from the linear regime can be valid for large perturbations, where nonlinear effects are expected to play a significant role. We encourage the authors to clarify the assumptions under which the linearized analysis remains valid and to discuss the potential limitations of applying these results to the nonlinear regime.

In this article, we address two main questions: first, which gene network topologies can give rise to non-trivial pattern transformations; and second, which broad types of resulting patterns can these gene network topologies give rise to resulting pattern. Thus, we are not intending to explain which exact resulting patterns would arise from any given gene network (i.e. a gene network topology with specific functions and interaction strengths or weights), a question for which non-linearities do indeed matter.

For most known gene regulatory networks, available empirical information is typically limited to the nature of gene product regulations -indicating whether they act as activators or inhibitors- while details about the specific functional form of these regulations are rare. For instance, given two gene products, i and j, the network may indicate that i acts as an activator of j, implying that the concentration of j increases with that of i. However, this increase could follow a variety of functional forms: it may be quadratic (e.g., ), cubic (e.g., ), or any other function f j(gi). As we explain in the description of our model, we restrict our study to functions with a monotonicity constraint: higher concentrations of i lead to increased production of j (i.e., ).  In other words, a given gene interaction is always inhibitory or activatory, it does not change of sign. This monotonicity constraint corresponds to requirement (R5) in our main text. This requirement it is based on the biologically plausible idea that the complexity of gene regulation in development stems more from the topology of gene networks than from the complexity of the regulation by which a gene product may regulate another (i.e. we use simple monotonic functions).

Question 1: A critical part to understand question 1 is in the dispersion relation that was explained in SI. From the reviewers’ comments it is clear that having this crucial part in the main text of an upcoming version of the article would improve understandability, specially for question 1.

In brief, any pattern transformation requires the initial pattern to change. The trigger of such change is a change in the concentration of some gene product, either conceptualized as a noise fluctuation (in the homogeneous initial pattern) or a regulated change in a specific point (in the spike initial pattern). Mathematically, both can be conceptualized as perturbations and, for pattern transformation to be possible, such perturbation should grow so that the initial pattern becomes unstable and can change to another resulting pattern.

If the perturbation is small, one can use the standard linear perturbation analysis in S6.2 of our Supplementary Information. In other words, the linear analysis is enough to ascertain if a small perturbation would grow or not. A gene network in which this will not happen would be unable to lead to pattern transformation, whichever the nonlinear part of f(g). In that sense, the linear approximation provides a necessary condition that any gene network needs to fulfill to lead to pattern transformation.

However, the linear analysis would not ascertain whether a specific gene network will actually lead to pattern transformation (i.e., the condition is not sufficient). This, as well as the shape of the specific resulting pattern, may actually depend on the non-linear parts too. As we discuss, based on the dispersion relation, and other complementing arguments along the article, we can also get some insights on the possible patterns from the linear approximation alone (question 2). This arguments hold thanks to the imposition of requirements (R1-R5) on function f(g), which prevent strange behaviors stemming from the nonlinear part of the equation.

The amplitude bound of perturbations mentioned by Reviewer #1 is addressed by requirements (R2) and (R4). Although the solution to the linear system predicts unbounded growth of unstable eigenmodes, the assume functions f(g) on which the nonlinear terms  eventually halt this growth, thereby ensuring the boundedness of solutions as imposed by (R4). This assumption on the nonlinear part is literally requirement R2 on f(g) in the main text.

The transitive chains and branchings in section S3 of the Supplementary Information mentioned by the Reviewer #2 are topological properties of gene networks and therefore they influence only the linear part of the reaction-diffusion equations. This is why the proofs in that section are based on the linearized equations. We agree that clarifying this point in the text, as suggested by the reviewer, would improve the reader’s understanding of the section.

Regarding Reviewer #2’s concerns about large perturbations, we acknowledge that the phrasing using “arbitrary height” may be confusing. For the homogeneous initial conditions these perturbations are assumed to be small because they are actually molecular noise (otherwise the initial condition could not be considered homogenous in the classical sense of developmental biology models). In the spike initial conditions in hierarchic networks the perturbation is not necessarily small. For the analysis provided in the SI we indeed assume that the perturbations are small enough for the linear approximation to be possible. Notice, however, that since these networks require an intracellular self-activating loop upstream of the first extracellular signal, the effective perturbation would rapidly grow to a value determined by such loop.

In general the height of the initial spike does not affect the fact that hierarchic networks can lead to non-trivial pattern transformation. By definition these networks require the secretion of an extracellular signal from the cells in the spike (otherwise no change in gene product concentrations can occur over space). By definition this signal is not produced by any other cells and, thus, its concentration is governed by diffusion from the spike and its production in the cells in the spike. Thus, whichever the initial height of the spike and whichever the non-linearities in f(g), the signal’s concentration would decrease with the distance from the spike. As explained in the main text, this would lead to non-trivial pattern transformations if other general conditions are met. In general, the height of the initial perturbation can affect which specific pattern transformation would arise from a specific gene network but not which gene network topologies can lead to pattern transformation. This will be more clearly stated in an upcoming version of the article. C. In the following, we respond to the remaining concerns raised by the reviewers:

Reviewer #1:

(1) The Results section is difficult to follow. Key logical steps and network configurations are described shortly in prose, which constantly require the reader to address either SI or other parts of the text (see numerous links on the requirements R1-R5 listed at the beginning of the paper) to gain minimal understanding. As a result, a scientifically literate but non-specialist reader may struggle to grasp the argument with a reasonable time invested.

We acknowledge that the current version of the main text may not be as clear as we intended. Initially, we believed that placing the more technical mathematical passages in the Supplementary Information would make the main text more accessible to readers. However, we agree with the reviewer that including some of these computations in the main text could improve clarity. We also believe that adding a summary table outlining all the model’s requirements would further contribute to that goal.

Reviewer #2:

(1) We have serious concerns regarding the validity of the simulation results presented in the manuscript. Rather than simulating the full nonlinear system described by Equation (1), the authors base their results on a truncated expansion (Equation S.8.2) that captures only the time evolution of small deviations around a spatially homogeneous steady state. However, it remains unclear how this reduced system is derived from the full equations specifically, which terms are retained or neglected and why- and how the expansion of the nonlinear function can be steady-state independent, as claimed. Additionally, in simulations involving the spike plus homogeneous initial condition, it is not evident -or, where equations are provided, it is not correct- that the assumed global homogeneous background actually corresponds to a steady state of the full dynamics. We elaborate on these concerns in the following:

We believe there has been a misunderstanding regarding the presentation of the model equations (S8.2) used throughout our simulations. Accordingly, we agree that this relevant section of the Supplementary Information should be rewritten in a revised version of the manuscript to clarify this issue. Below, we address all the concerns raised by the reviewer.

Equation (S8.2) represents the full nonlinear system described in Equation (1). While we recognize that the model may oversimplify real biological processes, its purpose is to illustrate our general statements about pattern formation rather than to capture any specific or detailed mechanism. In this context, model (S8.2) offers three key advantages for our goals: it allows rapid manipulation of gene network topology simply by modifying the matrix J, making it ideal for illustrating pattern formation across different network classes; it accommodates gene networks of arbitrary size -unlike other models, such as the classical Gierer-Meinhardt model, which are limited to two-element Turing or noise-amplifying networks-; and, due to the simplicity of its nonlinear terms, this model involves relatively few free parameters, facilitating the fine-tuning needed to identify parameter regions where non-trivial pattern transformations occur.

Indeed, we find that the ability of model (S8.2) to illustrate our results despite having such simple nonlinear terms -bearing in mind that at least some nonlinearity is always necessary for selforganization- strongly supports the claim that the capacity of a gene network to produce pattern transformations is fully determined by the linear part of Equation (1). In this sense, nonlinear terms primarily influence the precise parameter values at which these transformations occur and contribute to shaping specific features of the resulting patterns.

Model (S8.2) has been successfully employed in pattern formation studies elsewhere in the literature; accordingly, we provide relevant bibliographic references to support its widespread use.

We believe the misunderstanding arises from our explanation of the biological interpretation of the model. As noted in the accompanying bibliography, the model is based on a general reactiondiffusion mechanism assuming the existence of a steady state. However, this conceptual reactiondiffusion framework is not the same as our Equation (1); rather, it was introduced by the original proponents of the model in the seminal paper cited in our text. In this context, Equation (S8.2) describes small concentration perturbations around that steady state, where the variables represent deviations in concentration relative to the general steady state.

The aforementioned general steady state corresponds to the trivial equilibrium point g≡0 in equations (S8.2). Consequently, all our simulations based on model (S8.2) start from this steady state, to which we add white noise to generate homogeneous initial patterns or a sharp spike for the two types of spike initial patterns.

It is also worth noting that Equations (S8.2) represent a non-dimensional model.

It is assumed that the homogeneous steady states are given by g_i=0 and g_i=c_i, where 1/c_i = \mu_i or \hat{\mu}_i, independently of the specific network structure. However, the basis for this assumption is unclear, especially since some of the functions do not satisfy this condition -for example, f5 as defined below Eq. S8.10.5. Moreover, if g_i=c_i does not correspond to a true steady state, then the time evolution of deviations from this state is not correctly described by Eq. S8.2, as the zeroth-order terms do not vanish in that case.

From the explanations above, it is important to distinguish two scales in the process: the scale of small perturbations, where equations (S8.2) apply; and the global scale, where the conceptual general reaction-diffusion system operates. Since the specific form of this general system does not affect equations (S8.2), we assume that it follows any of the models cited in the text, which yield a non-zero steady state at .

In this sense, Equation (S8.2) represent a small concentration deviation of such global system and g(t ,x) is a relative concentration where g≡0 represents the steady-state at are concentrations above , and g<0 are concentrations below .

As previously mentioned, simulations are performed using Equations (S8.2) on the basis of the equilibrium point g≡0. The result of these simulations is then superimposed on the non-zero steady state and presented in the figures along the article.

Using the full model instead of the simplified Equations (S8.2) may result in slightly different resulting patterns, but it does not affect the gene network’s ability to produce pattern transformations, nor does it alter the main structural properties of the patterns—for example, the periodic nature of patterns generated by Turing networks.

Additionally, the equations used contain only linear terms and a cubic degradation term for each species g_i, while neglecting all quadratic terms and cubic terms involving cross-species interactions (i≠j). An explanation for this selective truncation is not provided, and without knowledge of the full equation (f), it is impossible to assess whether this expansion is mathematically justified. If, as suggested in the Supplementary Information, the linear and cubic terms are derived from f, then at the very least, the Jacobian matrix should depend on the background steady-state concentration. However, the equations for the small deviation around a steady state (including the Jacobian matrix) used in the simulations appear to be independent of the particular steady state concentration.

The Jacobian of Equation (S8.2) is independent of g because g represents a small perturbation around a steady state of a general reaction-diffusion system. Consequently, the matrix J corresponds to the Jacobian of the general system evaluated at that steady state. Evaluating the Jacobian of equations (S8.2) at the equilibrium point g≡0 -which represents the general steady state- recovers the matrix J.

This is why we believe that the differences observed between the spike-only initial condition and the spike superimposed on a homogeneous background are not due to the initial conditions themselves, but rather result from a modified reaction scheme introduced through a questionable cutoff.

"In simulations with spike initial patterns, the reference value g≡0 represents an actual concentration of 0 and therefore, we must add to (S8.2) a Heaviside function Φ acting of f (i.e., Φ(f(g))=f(g) if f(g)>0 , Φ(f(g))=0 if f(g){less than or equal to}0 ) to prevent the existence of negative concentrations for any gene product (i.e., g_i<0 for some i )." (SI chapter S8).

This cutoff alters the dynamics (no inhibition) and introduces a different reaction scheme between the two simulations. The need for this correction may itself reflect either a problem in the original equations (which should fulfill the necessary conditions and prevent negative concentrations (R4 in main text)) or the inappropriateness of using an expanded approximation which assumes independence on the steady state concentration. It is already questionable if the linearized equations with a cubic degradation term are valid for the spike initial conditions (with different background concentration values), as the amplitude of this perturbation seems rather large.

For homogeneous and spike+homogeneous initial conditions, we interpret equations (S8.2) as small perturbations around a non-zero steady state of a general reaction-diffusion system. For spike-only initial conditions, that steady state is zero. As we mention before, g≡0 will then represent such steady-state of zero concentration, g>0 are positive concentrations of the general system, and g<0 would represent unfeasible negative concentrations of the general system. Therefore, the use of a cutoff function to handle such initial conditions is justified. Moreover, this cutoff function is the same as the one employed in the reference general system cited in our paper.

We acknowledge that the cutoff influences the simulations and accounts for the differences observed between spike and spike+homogeneous initial conditions. However, this distinction reflects what occurs in real biological systems, which is precisely why we differentiate these two types of initial states. For instance, the emergence of a periodic pattern in a noise-amplifying network depends critically on the formation of regions with concentrations below the steady state near the initial spike. Such regions can form in spike-plus-homogeneous initial patterns but not in spike-only initial patterns, where concentrations below the steady state would correspond to biologically unfeasible negative values.

Lastly, we note that under the current simulation scheme, it is not possible to meaningfully assess criteria RH2a and RH2b, as they rely on nonlinear interactions that are absent from the implemented dynamics.

It is explicitly stated in the relevant subsections of Section S7 in the Supplementary Information that, for the simulations involving RH2a and RH2b, the function f(g) in equation (S8.2) is modified by adding an ad hoc quadratic term to enable the assessment of these criteria.

(3) Several statements in the main text are presented without accompanying proof or sufficient explanation, which makes it difficult to assess their validity. In some cases, the lack of justification raises serious doubts about whether the claims are generally true. Examples are:

"For the purpose of clarity we will explain our results as if these cells have a simple arrangement in space (e.g., a 1D line or a 2D square lattice) but, as we will discuss, our results shall apply with the same logic to any distribution of cells in space." (Main text l.145-l.148).

We believe that the confusion in this statement arises from the ambiguous use of the phrase “our results”. We will revise the text to provide a more precise description. Specifically, by “our results,” we refer to the conclusion that it is possible to determine whether a gene network leads to nontrivial pattern transformations based solely on its topology. This conclusion is independent of the dimensionality of space, as none of our arguments rely on assumptions specific to spatial dimensions. While one-dimensional examples are used for clarity and illustration, the underlying reasoning applies generally. In an improved version of the article, we will clarify this point explicitly and move relevant arguments from the Supplementary Information into the main text.

Critically, our classification of gene networks is ultimately based on an argument concerning the dispersion relation associated with the network, and the construction of this dispersion relation is independent of the spatial dimensionality of the domain. In this sense, the networks identified in the text as capable of producing pattern transformations will be able to generate non-trivial pattern transformations in any spatial domain and in any number of dimensions. While the specific parameter values that permit such transformations may vary depending on the geometry and dimensionality of the domain, the existence of at least one such parameter set remains unaffected.

The geometry of the domain can influence the specific form of the resulting patterns, but it does not alter the broader class of patterns (e.g., periodic patterns, peaks emerging around a spike, etc.) that a given gene network topology can produce. One such geometric influence, commonly observed in simulations, involves boundary effects. For example, structures such as peaks or rings forming near the boundaries may appear higher, broader, or spatially shifted compared to those arising in the central regions of the domain. However, we think a pattern consisting of a periodic train of peaks where only those near the boundary are slightly different can still be classified as a periodic pattern.

"For any non-trivial pattern transformation (as long as it is symmetric around the initial spike), there exists an H gene network capable of producing it from a spike initial pattern." (Main text l.366f).

A justification for this statement is provided shortly after the claim, although we acknowledge that the current explanation is somewhat cumbersome and would benefit from a clearer presentation in a revised version of the main text.

A more detailed justification is provided in the Supplementary Information, based on three key ideas. First, any pattern (provided it is symmetric with respect to the initial spike) can be described as an arrangement of peaks with varying heights and spatial positions along a one-dimensional domain. Second, there exists a simple gene network—the diamond network—that, through parameter tuning, can produce two peaks of arbitrary height and symmetric position relative to the initial spike. Third, by placing multiple diamond networks positively upstream of a common gene product, that gene product can express peaks at each location where the upstream diamond networks induce them. Under mild additional conditions, this mechanism allows the formation of essentially any symmetric pattern. These mild conditions, along with a detailed analysis of the diamond network’s ability to generate peaks with controllable height and position, are discussed in the Supplementary Information.

"In 2D there are no peaks but concentric rings of high gene product concentration centered around the spike, while in 3D there are concentric spherical shells." (Main text l. 447ff).

This result pertains specifically to pattern transformations arising from spike initial patterns. As defined in the text, spike initial patterns are radially symmetric. Since diffusion preserves radial symmetry, pattern transformations from spike initial patterns in two or three dimensions reduce to effectively one-dimensional transformations along each radial direction. In this framework, each pair of concentration peaks symmetric with respect to the spike in one dimension corresponds to a ring surrounding the spike in two dimensions, and each ring in two dimensions becomes a hollow spherical shell around the spike in three dimensions.

We agree that including a brief section in the Supplementary Information to clarify these subtleties would be helpful for readers to better understand the generalization of certain patterns to higher dimensions.

(4) The study identifies one-signal networks and examines how combinations of these structures can give rise to minimal pattern-forming subnetworks. However, the analysis of the combinations of these minimal pattern-forming subnetworks remains relatively brief, and the manuscript does not explore how the results might change if the subnetworks were combined in upstream and downstream configurations. In our view, it is not evident that all possible gene regulatory networks can be fully characterized by these categories, nor that the resulting patterns can be reliably predicted. Rather, the approach appears more suited to identifying which known subnetworks are present within a larger network, without necessarily capturing the full dynamics of more complex configurations.

We acknowledge that our explanation regarding the combination of sub-networks was relatively brief, and we intend to address this in a revised version. Our argument that combining sub-networks does not produce qualitatively new types of pattern transformations -beyond those already described- is based on the dispersion relation. Although this relation was only detailed in the Supplementary Information, it is central to our argument and will therefore be moved to the main text. Below, we provide an outline of this argument:

Our study identifies two distinct behaviors of the principal branch of the dispersion relation at large wavenumbers. Based on this, gene networks capable of pattern formation can be classified into two categories: networks of the first kind, where the real part of the principal branch diverges to infinity as the wavenumber increases; and networks of the second kind, where the real part of the principal branch converges to a positive finite value for large wavenumbers. Naturally this argument applies to any gene network irrespectively of which, or how many, sub-networks are used to built it.

Any gene regulatory network capable of pattern formation falls into one of these two categories. We identified that networks of the first kind contain at least one Turing sub-network, whereas networks of the second kind include either an H sub-network or a noise-amplifying sub-network. In this way, the primary objective of our study -namely, achieving a topological classification of gene regulatory networks capable of pattern formation- is fulfilled. It is important to note that while the dispersion relation provides broad information about the possible resulting patterns a gene network topology can produce (e.g., periodic versus noisy), it does not specify the exact patterns that emerge for each particular set of parameter values.

Finally, regarding the shape of the resulting patterns, Figure S10 in the Supplementary Information exemplifies the notion that the behavior of combined networks can be understood as a combination of the individual behaviors of each constituent sub-network (note that the contribution of each type of sub-network in the resulting pattern is readily distinguishable). Consequently, we focus our detailed analysis on the patterning properties of the fundamental classes.

(6) The manuscript lacks a clear and detailed explanation of the underlying model and its assumptions. In particular, it is not well-defined what constitutes a "cell" in the context of the model, nor is it justified why spatial features of cells -such as their size or boundaries- can be neglected. Furthermore, the concept of the extracellular space in the one-dimensional model remains ambiguous, making it unclear which gene products are assumed to diffuse.

The size of cells is ignored in our model because we assume that they are small enough with respect to the total size of the domain that the space continuous reaction-diffusion equation (equation (1) in the main text) holds. Conceptually, one could understand cells in our model each of the pieces in an even partition of the domain into small subdomains surrounding each position x. This is anyway the standard procedure in most models of pattern formation by reaction-diffusion in embryonic development.

For extracellular signals, we assume that g(t ,x) corresponds to the concentration of the signal in the extracellular space surrounding the cell located at position x. The extracellular space is any fluid medium for which Fick Laws apply and, therfore, the Fickian diffusion term in equation (1) is valid.

For intracellular gene products, we assume that g(t ,x) corresponds to the concentration of such gene product within the cell at position x (if the gene product in hand is a transcription factor, for example), or on its surface (if it is a membrane-bound receptor). When collapsed in the continuous equations there is not such difference between being strictly within the cell or on its boundary. The only important fact is that these gene products cannot diffuse.

Regarding cell boundaries, let us consider an extracellular signal s that regulates a transcriptor factor i within cells (in our model, i is an intracellular gene product). Such regulation shall be mediated by a membrane-bound receptor, which corresponds to intracellular gene product j. In terms of the gene regulatory network this is s→ j→i. Cell boundary effects mentioned by the reviewer should be encapsulated in the specific functional form of the regulation function f(g), but they have no effect in the actual topology of the network. Consequently, they are out of the scope of this study: as we mentioned before, considering different non-linear terms for f(g) will affect the parameter range for which a gene network is capable of producing non-trivial pattern transformations, but not their overall ability to produce non-trivial pattern transformations (i.e., the existence of at least one choice of model parameters for which such transformations take place).

Finally, we would like to once again express our sincere gratitude to all reviewers for their insightful and constructive feedback. We are confident that the thorough peer review process will significantly enhance both the clarity and depth of our work. We greatly value the detailed comments provided and will carefully incorporate them in the preparation of a revised manuscript, which we intend to submit in the coming months.

Author response:

eLife Assessment 

This valuable study investigates how the neural representation of individual finger movements changes during the early period of sequence learning. By combining a new method for extracting features from human magnetoencephalography data and decoding analyses, the authors provide incomplete evidence of an early, swift change in the brain regions correlated with sequence learning, including a set of previously unreported frontal cortical regions. The addition of more control analyses to rule out that head movement artefacts influence the findings, and to further explain the proposal of offline contextualization during short rest periods as the basis for improvement performance would strengthen the manuscript. 

We appreciate the Editorial assessment on our paper’s strengths and novelty.  We have implemented additional control analyses to show that neither task-related eye movements nor increasing overlap of finger movements during learning account for our findings, which are that contextualized neural representations in a network of bilateral frontoparietal brain regions actively contribute to skill learning.  Importantly, we carried out additional analyses showing that contextualization develops predominantly during rest intervals.

Public Reviews:

We thank the Reviewers for their comments and suggestions, prompting new analyses and additions that strengthened our report.

Reviewer #1 (Public review): 

Summary: 

This study addresses the issue of rapid skill learning and whether individual sequence elements (here: finger presses) are differentially represented in human MEG data. The authors use a decoding approach to classify individual finger elements and accomplish an accuracy of around 94%. A relevant finding is that the neural representations of individual finger elements dynamically change over the course of learning. This would be highly relevant for any attempts to develop better brain machine interfaces - one now can decode individual elements within a sequence with high precision, but these representations are not static but develop over the course of learning. 

Strengths: The work follows a large body of work from the same group on the behavioural and neural foundations of sequence learning. The behavioural task is well established and neatly designed to allow for tracking learning and how individual sequence elements contribute. The inclusion of short offline rest periods between learning epochs has been influential because it has revealed that a lot, if not most of the gains in behaviour (ie speed of finger movements) occur in these so-called micro-offline rest periods. The authors use a range of new decoding techniques, and exhaustively interrogate their data in different ways, using different decoding approaches. Regardless of the approach, impressively high decoding accuracies are observed, but when using a hybrid approach that combines the MEG data in different ways, the authors observe decoding accuracies of individual sequence elements from the MEG data of up to 94%. 

We have previously showed that neural replay of MEG activity representing the practiced skill correlated with micro-offline gains during rest intervals of early learning, 1 consistent with the recent report that hippocampal ripples during these offline periods predict human motor sequence learning2.  However, decoding accuracy in our earlier work1 needed improvement.  Here, we reported a strategy to improve decoding accuracy that could benefit future studies of neural replay or BCI using MEG.

Weaknesses: 

There are a few concerns which the authors may well be able to resolve. These are not weaknesses as such, but factors that would be helpful to address as these concern potential contributions to the results that one would like to rule out. Regarding the decoding results shown in Figure 2 etc, a concern is that within individual frequency bands, the highest accuracy seems to be within frequencies that match the rate of keypresses. This is a general concern when relating movement to brain activity, so is not specific to decoding as done here. As far as reported, there was no specific restraint to the arm or shoulder, and even then it is conceivable that small head movements would correlate highly with the vigor of individual finger movements. This concern is supported by the highest contribution in decoding accuracy being in middle frontal regions - midline structures that would be specifically sensitive to movement artefacts and don't seem to come to mind as key structures for very simple sequential keypress tasks such as this - and the overall pattern is remarkably symmetrical (despite being a unimanual finger task) and spatially broad. This issue may well be matching the time course of learning, as the vigor and speed of finger presses will also influence the degree to which the arm/shoulder and head move. This is not to say that useful information is contained within either of the frequencies or broadband data. But it raises the question of whether a lot is dominated by movement "artefacts" and one may get a more specific answer if removing any such contributions. 

Reviewer #1 expresses concern that the combination of the low-frequency narrow-band decoder results, and the bilateral middle frontal regions displaying the highest average intra-parcel decoding performance across subjects is suggestive that the decoding results could be driven by head movement or other artefacts.

Head movement artefacts are highly unlikely to contribute meaningfully to our results for the following reasons. First, in addition to ICA denoising, all “recordings were visually inspected and marked to denoise segments containing other large amplitude artifacts due to movements” (see Methods). Second, the response pad was positioned in a manner that minimized wrist, arm or more proximal body movements during the task. Third, while head position was not monitored online for this study, the head was restrained using an inflatable air bladder, and head position was assessed at the beginning and at the end of each recording. Head movement did not exceed 5mm between the beginning and end of each scan for all participants included in the study. Fourth, we agree that despite the steps taken above, it is possible that minor head movements could still contribute to some remaining variance in the MEG data in our study. The Reviewer states a concern that “it is conceivable that small head movements would correlate highly with the vigor of individual finger movements”. However, in order for any such correlations to meaningfully impact decoding performance, such head movements would need to: (A) be consistent and pervasive throughout the recording (which might not be the case if the head movements were related to movement vigor and vigor changed over time); and (B) systematically vary between different finger movements, and also between the same finger movement performed at different sequence locations (see 5-class decoding performance in Figure 4B). The possibility of any head movement artefacts meeting all these conditions is extremely unlikely.

Given the task design, a much more likely confound in our estimation would be the contribution of eye movement artefacts to the decoder performance (an issue appropriately raised by Reviewer #3 in the comments below). Remember from Figure 1A in the manuscript that an asterisk marks the current position in the sequence and is updated at each keypress. Since participants make very few performance errors, the position of the asterisk on the display is highly correlated with the keypress being made in the sequence. Thus, it is possible that if participants are attending to the visual feedback provided on the display, they may move their eyes in a way that is systematically related to the task.  Since we did record eye movements simultaneously with the MEG recordings (EyeLink 1000 Plus; Fs = 600 Hz), we were able to perform a control analysis to address this question. For each keypress event during trials in which no errors occurred (which is the same time-point that the asterisk position is updated), we extracted three features related to eye movements: 1) the gaze position at the time of asterisk position update (or keyDown event), 2) the gaze position 150ms later, and 3) the peak velocity of the eye movement between the two positions. We then constructed a classifier from these features with the aim of predicting the location of the asterisk (ordinal positions 1-5) on the display. As shown in the confusion matrix below (Author response image 1), the classifier failed to perform above chance levels (Overall cross-validated accuracy = 0.21817):

Author response image 1.

Confusion matrix showing that three eye movement features fail to predict asterisk position on the task display above chance levels (Fold 1 test accuracy = 0.21718; Fold 2 test accuracy = 0.22023; Fold 3 test accuracy = 0.21859; Fold 4 test accuracy = 0.22113; Fold 5 test accuracy = 0.21373; Overall cross-validated accuracy = 0.2181). Since the ordinal position of the asterisk on the display is highly correlated with the ordinal position of individual keypresses in the sequence, this analysis provides strong evidence that keypress decoding performance from MEG features is not explained by systematic relationships between finger movement behavior and eye movements (i.e. – behavioral artefacts).

In fact, inspection of the eye position data revealed that a majority of participants on most trials displayed random walk gaze patterns around a center fixation point, indicating that participants did not attend to the asterisk position on the display. This is consistent with intrinsic generation of the action sequence, and congruent with the fact that the display does not provide explicit feedback related to performance. A similar real-world example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks), which is typically ignored by the user. The minimal participant engagement with the visual task display observed in this study highlights another important point – that the behavior in explicit sequence learning motor tasks is highly generative in nature rather than reactive to stimulus cues as in the serial reaction time task (SRTT).  This is a crucial difference that must be carefully considered when designing investigations and comparing findings across studies.

We observed that initial keypress decoding accuracy was predominantly driven by contralateral primary sensorimotor cortex in the initial practice trials before transitioning to bilateral frontoparietal regions by trials 11 or 12 as performance gains plateaued.  The contribution of contralateral primary sensorimotor areas to early skill learning has been extensively reported in humans and non-human animals. 1,3-5  Similarly, the increased involvement of bilateral frontal and parietal regions to decoding during early skill learning in the non-dominant hand is well known.  Enhanced bilateral activation in both frontal and parietal cortex during skill learning has been extensively reported6-11, and appears to be even more prominent during early fine motor skill learning in the non-dominant hand12,13.  The frontal regions identified in these studies are known to play crucial roles in executive control14, motor planning15, and working memory6,8,16-18 processes, while the same parietal regions are known to integrate multimodal sensory feedback and support visuomotor transformations6,8,16-18, in addition to working memory19. Thus, it is not surprising that these regions increasingly contribute to decoding as subjects internalize the sequential task.  We now include a statement reflecting these considerations in the revised Discussion.

A somewhat related point is this: when combining voxel and parcel space, a concern is whether a degree of circularity may have contributed to the improved accuracy of the combined data, because it seems to use the same MEG signals twice - the voxels most contributing are also those contributing most to a parcel being identified as relevant, as parcels reflect the average of voxels within a boundary. In this context, I struggled to understand the explanation given, ie that the improved accuracy of the hybrid model may be due to "lower spatially resolved whole-brain and higher spatially resolved regional activity patterns".

We strongly disagree with the Reviewer’s assertion that the construction of the hybrid-space decoder is circular. To clarify, the base feature set for the hybrid-space decoder constructed for all participants includes whole-brain spatial patterns of MEG source activity averaged within parcels. As stated in the manuscript, these 148 inter-parcel features reflect “lower spatially resolved whole-brain activity patterns” or global brain dynamics. We then independently test how well spatial patterns of MEG source activity for all voxels distributed within individual parcels can decode keypress actions. Again, the testing of these intra-parcel spatial patterns, intended to capture “higher spatially resolved regional brain activity patterns”, is completely independent from one another and independent from the weighting of individual inter-parcel features. These intra-parcel features could, for example, provide additional information about muscle activation patterns or the task environment. These approximately 1150 intra-parcel voxels (on average, within the total number varying between subjects) are then combined with the 148 inter-parcel features to construct the final hybrid-space decoder. In fact, this varied spatial filter approach shares some similarities to the construction of convolutional neural networks (CNNs) used to perform object recognition in image classification applications. One could also view this hybrid-space decoding approach as a spatial analogue to common time-frequency based analyses such as theta-gamma phase amplitude coupling (PAC), which combine information from two or more narrow-band spectral features derived from the same time-series data.

We directly tested this hypothesis – that spatially overlapping intra- and inter-parcel features portray different information – by constructing an alternative hybrid-space decoder (HybridAlt) that excluded average inter-parcel features which spatially overlapped with intra-parcel voxel features, and comparing the performance to the decoder used in the manuscript (HybridOrig). The prediction was that if the overlapping parcel contained similar information to the more spatially resolved voxel patterns, then removing the parcel features (n=8) from the decoding analysis should not impact performance. In fact, despite making up less than 1% of the overall input feature space, removing those parcels resulted in a significant drop in overall performance greater than 2% (78.15% ± SD 7.03% for HybridOrig vs. 75.49% ± SD 7.17% for HybridAlt; Wilcoxon signed rank test, z = 3.7410, p = 1.8326e-04) (Author response image 2).

Author response image 2.

Comparison of decoding performances with two different hybrid approaches. HybridAlt: Intra-parcel voxel-space features of top ranked parcels and inter-parcel features of remaining parcels. HybridOrig:  Voxel-space features of top ranked parcels and whole-brain parcel-space features (i.e. – the version used in the manuscript). Dots represent decoding accuracy for individual subjects. Dashed lines indicate the trend in performance change across participants. Note, that HybridOrig (the approach used in our manuscript) significantly outperforms the HybridAlt approach, indicating that the excluded parcel features provide unique information compared to the spatially overlapping intra-parcel voxel patterns.

Firstly, there will be a relatively high degree of spatial contiguity among voxels because of the nature of the signal measured, i.e. nearby individual voxels are unlikely to be independent. Secondly, the voxel data gives a somewhat misleading sense of precision; the inversion can be set up to give an estimate for each voxel, but there will not just be dependence among adjacent voxels, but also substantial variation in the sensitivity and confidence with which activity can be projected to different parts of the brain. Midline and deeper structures come to mind, where the inversion will be more problematic than for regions along the dorsal convexity of the brain, and a concern is that in those midline structures, the highest decoding accuracy is seen. 

We definitely agree with the Reviewer that some inter-parcel features representing neighboring (or spatially contiguous) voxels are likely to be correlated. This has been well documented in the MEG literature20,21 and is a particularly important confound to address in functional or effective connectivity analyses (not performed in the present study). In the present analysis, any correlation between adjacent voxels presents a multi-collinearity problem, which effectively reduces the dimensionality of the input feature space. However, as long as there are multiple groups of correlated voxels within each parcel (i.e. - the effective dimensionality is still greater than 1), the intra-parcel spatial patterns could still meaningfully contribute to the decoder performance. Two specific results support this assertion.

First, we obtained higher decoding accuracy with voxel-space features [74.51% (± SD 7.34%)] compared to parcel space features [68.77% (± SD 7.6%)] (Figure 3B), indicating individual voxels carry more information in decoding the keypresses than the averaged voxel-space features or parcel-space features.  Second, Individual voxels within a parcel showed varying feature importance scores in decoding keypresses (Author response image 3). This finding supports the Reviewer’s assertion that neighboring voxels express similar information, but also shows that the correlated voxels form mini subclusters that are much smaller spatially than the parcel they reside in.

Author response image 3.

Feature importance score of individual voxels in decoding keypresses: MRMR was used to rank the individual voxel space features in decoding keypresses and the min-max normalized MRMR score was mapped to a structural brain surface. Note that individual voxels within a parcel showed different contribution to decoding.

Some of these concerns could be addressed by recording head movement (with enough precision) to regress out these contributions. The authors state that head movement was monitored with 3 fiducials, and their time courses ought to provide a way to deal with this issue. The ICA procedure may not have sufficiently dealt with removing movement-related problems, but one could eg relate individual components that were identified to the keypresses as another means for checking. An alternative could be to focus on frequency ranges above the movement frequencies. The accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment. 

We have already addressed the issue of movement related artefacts in the first response above. With respect to a focus on frequency ranges above movement frequencies, the Reviewer states the “accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment”. First, it is important to note that cortical delta-band oscillations measured with local field potentials (LFPs) in macaques is known to contain important information related to end-effector kinematics22,23 muscle activation patterns24 and temporal sequencing25 during skilled reaching and grasping actions. Thus, there is a substantial body of evidence that low-frequency neural oscillatory activity in this range contains important information about the skill learning behavior investigated in the present study. Second, our own data shows (which the Reviewer also points out) that significant information related to the skill learning behavior is also present in higher frequency bands (see Figure 2A and Figure 3—figure supplement 1). As we pointed out in our earlier response to questions about the hybrid space decoder architecture (see above), it is likely that different, yet complimentary, information is encoded across different temporal frequencies (just as it is encoded across different spatial frequencies). Again, this interpretation is supported by our data as the highest performing classifiers in all cases (when holding all parameters constant) were always constructed from broadband input MEG data (Figure 2A and Figure 3—figure supplement 1).  

One question concerns the interpretation of the results shown in Figure 4. They imply that during the course of learning, entirely different brain networks underpin the behaviour. Not only that, but they also include regions that would seem rather unexpected to be key nodes for learning and expressing relatively simple finger sequences, such as here. What then is the biological plausibility of these results? The authors seem to circumnavigate this issue by moving into a distance metric that captures the (neural network) changes over the course of learning, but the discussion seems detached from which regions are actually involved; or they offer a rather broad discussion of the anatomical regions identified here, eg in the context of LFOs, where they merely refer to "frontoparietal regions". 

The Reviewer notes the shift in brain networks driving keypress decoding performance between trials 1, 11 and 36 as shown in Figure 4A. The Reviewer questions whether these substantial shifts in brain network states underpinning the skill are biologically plausible, as well as the likelihood that bilateral superior and middle frontal and parietal cortex are important nodes within these networks.

First, previous fMRI work in humans performing a similar sequence learning task showed that flexibility in brain network composition (i.e. – changes in brain region members displaying coordinated activity) is up-regulated in novel learning environments and explains differences in learning rates across individuals26.  This work supports our interpretation of the present study data, that brain networks engaged in sequential motor skills rapidly reconfigure during early learning.

Second, frontoparietal network activity is known to support motor memory encoding during early learning27,28. For example, reactivation events in the posterior parietal29 and medial prefrontal30,31 cortex (MPFC) have been temporally linked to hippocampal replay, and are posited to support memory consolidation across several memory domains32, including motor sequence learning1,33,34.  Further, synchronized interactions between MPFC and hippocampus are more prominent during early learning as opposed to later stages27,35,36, perhaps reflecting “redistribution of hippocampal memories to MPFC” 27.  MPFC contributes to very early memory formation by learning association between contexts, locations, events and adaptive responses during rapid learning37. Consistently, coupling between hippocampus and MPFC has been shown during, and importantly immediately following (rest) initial memory encoding38,39.  Importantly, MPFC activity during initial memory encoding predicts subsequent recall40. Thus, the spatial map required to encode a motor sequence memory may be “built under the supervision of the prefrontal cortex” 28, also engaged in the development of an abstract representation of the sequence41.  In more abstract terms, the prefrontal, premotor and parietal cortices support novice performance “by deploying attentional and control processes” 42-44 required during early learning42-44. The dorsolateral prefrontal cortex DLPFC specifically is thought to engage in goal selection and sequence monitoring during early skill practice45, all consistent with the schema model of declarative memory in which prefrontal cortices play an important role in encoding46,47.  Thus, several prefrontal and frontoparietal regions contributing to long term learning 48 are also engaged in early stages of encoding. Altogether, there is strong biological support for the involvement of bilateral prefrontal and frontoparietal regions to decoding during early skill learning.  We now address this issue in the revised manuscript.

If I understand correctly, the offline neural representation analysis is in essence the comparison of the last keypress vs the first keypress of the next sequence. In that sense, the activity during offline rest periods is actually not considered. This makes the nomenclature somewhat confusing. While it matches the behavioural analysis, having only key presses one can't do it in any other way, but here the authors actually do have recordings of brain activity during offline rest. So at the very least calling it offline neural representation is misleading to this reviewer because what is compared is activity during the last and during the next keypress, not activity during offline periods. But it also seems a missed opportunity - the authors argue that most of the relevant learning occurs during offline rest periods, yet there is no attempt to actually test whether activity during this period can be useful for the questions at hand here. 

We agree with the Reviewer that our previous “offline neural representation” nomenclature could be misinterpreted. In the revised manuscript we refer to this difference as the “offline neural representational change”. Please, note that our previous work did link offline neural activity (i.e. – 16-22 Hz beta power and neural replay density during inter-practice rest periods) to observed micro-offline gains49.

Reviewer #2 (Public review): 

Summary 

Dash et al. asked whether and how the neural representation of individual finger movements is "contextualized" within a trained sequence during the very early period of sequential skill learning by using decoding of MEG signal. Specifically, they assessed whether/how the same finger presses (pressing index finger) embedded in the different ordinal positions of a practiced sequence (4-1-3-2-4; here, the numbers 1 through 4 correspond to the little through the index fingers of the non-dominant left hand) change their representation (MEG feature). They did this by computing either the decoding accuracy of the index finger at the ordinal positions 1 vs. 5 (index_OP1 vs index_OP5) or pattern distance between index_OP1 vs. index_OP5 at each training trial and found that both the decoding accuracy and the pattern distance progressively increase over the course of learning trials. More interestingly, they also computed the pattern distance for index_OP5 for the last execution of a practice trial vs. index_OP1 for the first execution in the next practice trial (i.e., across the rest period). This "off-line" distance was significantly larger than the "on-line" distance, which was computed within practice trials and predicted micro-offline skill gain. Based on these results, the authors conclude that the differentiation of representation for the identical movement embedded in different positions of a sequential skill ("contextualization") primarily occurs during early skill learning, especially during rest, consistent with the recent theory of the "micro-offline learning" proposed by the authors' group. I think this is an important and timely topic for the field of motor learning and beyond. <br /> Strengths 

The specific strengths of the current work are as follows. First, the use of temporally rich neural information (MEG signal) has a large advantage over previous studies testing sequential representations using fMRI. This allowed the authors to examine the earliest period (= the first few minutes of training) of skill learning with finer temporal resolution. Second, through the optimization of MEG feature extraction, the current study achieved extremely high decoding accuracy (approx. 94%) compared to previous works. As claimed by the authors, this is one of the strengths of the paper (but see my comments). Third, although some potential refinement might be needed, comparing "online" and "offline" pattern distance is a neat idea. 

Weaknesses 

Along with the strengths I raised above, the paper has some weaknesses. First, the pursuit of high decoding accuracy, especially the choice of time points and window length (i.e., 200 msec window starting from 0 msec from key press onset), casts a shadow on the interpretation of the main result. Currently, it is unclear whether the decoding results simply reflect behavioral change or true underlying neural change. As shown in the behavioral data, the key press speed reached 3~4 presses per second already at around the end of the early learning period (11th trial), which means inter-press intervals become as short as 250-330 msec. Thus, in almost more than 60% of training period data, the time window for MEG feature extraction (200 msec) spans around 60% of the inter-press intervals. Considering that the preparation/cueing of subsequent presses starts ahead of the actual press (e.g., Kornysheva et al., 2019) and/or potential online planning (e.g., Ariani and Diedrichsen, 2019), the decoder likely has captured these future press information as well as the signal related to the current key press, independent of the formation of genuine sequential representation (e.g., "contextualization" of individual press). This may also explain the gradual increase in decoding accuracy or pattern distance between index_OP1 vs. index_OP5 (Figure 4C and 5A), which co-occurred with performance improvement, as shorter inter-press intervals are more favorable for the dissociating the two index finger presses followed by different finger presses. The compromised decoding accuracies for the control sequences can be explained in similar logic. Therefore, more careful consideration and elaborated discussion seem necessary when trying to both achieve high-performance decoding and assess early skill learning, as it can impact all the subsequent analyses.

The Reviewer raises the possibility that (given the windowing parameters used in the present study) an increase in “contextualization” with learning could simply reflect faster typing speeds as opposed to an actual change in the underlying neural representation. The issue can essentially be framed as a mixing problem. As correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged (assuming this mixing of representations is used by the classifier to differentially tag each index finger press). If this were the case, it follows that such mixing effects reflecting the ordinal sequence structure would also be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A in the previously submitted manuscript do not show this trend in the distribution of misclassifications across the four fingers.

Moreover, if the representation distance is largely driven by this mixing effect, it’s also possible that the increased overlap between consecutive index finger keypresses during the 4-4 transition marking the end of one sequence and the beginning of the next one could actually mask contextualization-related changes to the underlying neural representations and make them harder to detect. In this case, a decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position might show decreased performance with learning as adjacent keypresses overlapped in time with each other to an increasing extent. However, Figure 4C in our previously submitted manuscript does not support this possibility, as the 2-class hybrid classifier displays improved classification performance over early practice trials despite greater temporal overlap.

We also conducted a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis affirmed that the possible alternative explanation put forward by the Reviewer is not supported by our data (Adjusted R2 = 0.00431; F = 5.62). We now include this new negative control analysis result in the revised manuscript.

Overall, we do strongly agree with the Reviewer that the naturalistic, self-paced, generative task employed in the present study results in overlapping brain processes related to planning, execution, evaluation and memory of the action sequence. We also agree that there are several tradeoffs to consider in the construction of the classifiers depending on the study aim. Given our aim of optimizing keypress decoder accuracy in the present study, the set of trade-offs resulted in representations reflecting more the latter three processes, and less so the planning component. Whether separate decoders can be constructed to tease apart the representations or networks supporting these overlapping processes is an important future direction of research in this area. For example, work presently underway in our lab constrains the selection of windowing parameters in a manner that allows individual classifiers to be temporally linked to specific planning, execution, evaluation or memory-related processes to discern which brain networks are involved and how they adaptively reorganize with learning. Results from the present study (Figure 4—figure supplement 2) showing hybrid-space decoder prediction accuracies exceeding 74% for temporal windows spanning as little as 25ms and located up to 100ms prior to the keyDown event strongly support the feasibility of such an approach.

Related to the above point, testing only one particular sequence (4-1-3-2-4), aside from the control ones, limits the generalizability of the finding. This also may have contributed to the extremely high decoding accuracy reported in the current study. 

The Reviewer raises a question about the generalizability of the decoder accuracy reported in our study. Fortunately, a comparison between decoder performances on Day 1 and Day 2 datasets does provide some insight into this issue. As the Reviewer points out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4-class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3—supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. Both changes in accuracy are important with regards to the generalizability of our findings. First, 87.11% performance accuracy for the trained sequence data on Day 2 (a reduction of only 3.36%) indicates that the hybrid-space decoder performance is robust over multiple MEG sessions, and thus, robust to variations in SNR across the MEG sensor array caused by small differences in head position between scans.  This indicates a substantial advantage over sensor-space decoding approaches. Furthermore, when tested on data from unpracticed sequences, overall performance dropped an additional 7.67%. This difference reflects the performance bias of the classifier for the trained sequence, possibly caused by high-order sequence structure being incorporated into the feature weights. In the future, it will be important to understand in more detail how random or repeated keypress sequence training data impacts overall decoder performance and generalization. We strongly agree with the Reviewer that the issue of generalizability is extremely important and have added a new paragraph to the Discussion in the revised manuscript highlighting the strengths and weaknesses of our study with respect to this issue.

In terms of clinical BCI, one of the potential relevance of the study, as claimed by the authors, it is not clear that the specific time window chosen in the current study (up to 200 msec since key press onset) is really useful. In most cases, clinical BCI would target neural signals with no overt movement execution due to patients' inability to move (e.g., Hochberg et al., 2012). Given the time window, the surprisingly high performance of the current decoder may result from sensory feedback and/or planning of subsequent movement, which may not always be available in the clinical BCI context. Of course, the decoding accuracy is still much higher than chance even when using signal before the key press (as shown in Figure 4 Supplement 2), but it is not immediately clear to me that the authors relate their high decoding accuracy based on post-movement signal to clinical BCI settings.

The Reviewer questions the relevance of the specific window parameters used in the present study for clinical BCI applications, particularly for paretic patients who are unable to produce finger movements or for whom afferent sensory feedback is no longer intact. We strongly agree with the Reviewer that any intended clinical application must carefully consider these specific input feature constraints dictated by the clinical cohort, and in turn impose appropriate and complimentary constraints on classifier parameters that may differ from the ones used in the present study.  We now highlight this issue in the Discussion of the revised manuscript and relate our present findings to published clinical BCI work within this context.

One of the important and fascinating claims of the current study is that the "contextualization" of individual finger movements in a trained sequence specifically occurs during short rest periods in very early skill learning, echoing the recent theory of micro-offline learning proposed by the authors' group. Here, I think two points need to be clarified. First, the concept of "contextualization" is kept somewhat blurry throughout the text. It is only at the later part of the Discussion (around line #330 on page 13) that some potential mechanism for the "contextualization" is provided as "what-and-where" binding. Still, it is unclear what "contextualization" actually is in the current data, as the MEG signal analyzed is extracted from 0-200 msec after the keypress. If one thinks something is contextualizing an action, that contextualization should come earlier than the action itself. 

The Reviewer requests that we: 1) more clearly define our use of the term “contextualization” and 2) provide the rationale for assessing it over a 200ms window aligned to the keyDown event. This choice of window parameters means that the MEG activity used in our analysis was coincident with, rather than preceding, the actual keypresses.  We define contextualization as the differentiation of representation for the identical movement embedded in different positions of a sequential skill. That is, representations of individual action elements progressively incorporate information about their relationship to the overall sequence structure as the skill is learned. We agree with the Reviewer that this can be appropriately interpreted as “what-and-where” binding. We now incorporate this definition in the Introduction of the revised manuscript as requested.

The window parameters for optimizing accurate decoding individual finger movements were determined using a grid search of the parameter space (a sliding window of variable width between 25-350 ms with 25 ms increments variably aligned from 0 to +100ms with 10ms increments relative to the keyDown event). This approach generated 140 different temporal windows for each keypress for each participant, with the final parameter selection determined through comparison of the resulting performance between each decoder.  Importantly, the decision to optimize for decoding accuracy placed an emphasis on keypress representations characterized by the most consistent and robust features shared across subjects, which in turn maximize statistical power in detecting common learning-related changes. In this case, the optimal window encompassed a 200ms epoch aligned to the keyDown event (t0 = 0 ms).  We then asked if the representations (i.e. – spatial patterns of combined parcel- and voxel-space activity) of the same digit at two different sequence positions changed with practice within this optimal decoding window.  Of course, our findings do not rule out the possibility that contextualization can also be found before or even after this time window, as we did not directly address this issue in the present study.  Ongoing work in our lab, as pointed out above, is investigating contextualization within different time windows tailored specifically for assessing sequence skill action planning, execution, evaluation and memory processes.

The second point is that the result provided by the authors is not yet convincing enough to support the claim that "contextualization" occurs during rest. In the original analysis, the authors presented the statistical significance regarding the correlation between the "offline" pattern differentiation and micro-offline skill gain (Figure 5. Supplement 1), as well as the larger "offline" distance than "online" distance (Figure 5B). However, this analysis looks like regressing two variables (monotonically) increasing as a function of the trial. Although some information in this analysis, such as what the independent/dependent variables were or how individual subjects were treated, was missing in the Methods, getting a statistically significant slope seems unsurprising in such a situation. Also, curiously, the same quantitative evidence was not provided for its "online" counterpart, and the authors only briefly mentioned in the text that there was no significant correlation between them. It may be true looking at the data in Figure 5A as the online representation distance looks less monotonically changing, but the classification accuracy presented in Figure 4C, which should reflect similar representational distance, shows a more monotonic increase up to the 11th trial. Further, the ways the "online" and "offline" representation distance was estimated seem to make them not directly comparable. While the "online" distance was computed using all the correct press data within each 10 sec of execution, the "offline" distance is basically computed by only two presses (i.e., the last index_OP5 vs. the first index_OP1 separated by 10 sec of rest). Theoretically, the distance between the neural activity patterns for temporally closer events tends to be closer than that between the patterns for temporally far-apart events. It would be fairer to use the distance between the first index_OP1 vs. the last index_OP5 within an execution period for "online" distance, as well. 

The Reviewer suggests that the current data is not convincing enough to show that contextualization occurs during rest and raises two important concerns: 1) the relationship between online contextualization and micro-online gains is not shown, and 2) the online distance was calculated differently from its offline counterpart (i.e. - instead of calculating the distance between last IndexOP5 and first IndexOP1 from a single trial, the distance was calculated for each sequence within a trial and then averaged).

We addressed the first concern by performing individual subject correlations between 1) contextualization changes during rest intervals and micro-offline gains; 2) contextualization changes during practice trials and micro-online gains, and 3) contextualization changes during practice trials and micro-offline gains (Author response image 4). We then statistically compared the resulting correlation coefficient distributions and found that within-subject correlations for contextualization changes during rest intervals and micro-offline gains were significantly higher than online contextualization and micro-online gains (t = 3.2827, p = 0.0015) and online contextualization and micro-offline gains (t = 3.7021, p = 5.3013e-04). These results are consistent with our interpretation that micro-offline gains are supported by contextualization changes during the inter-practice rest period.

Author response image 4.

Distribution of individual subject correlation coefficients between contextualization changes occurring during practice or rest with  micro-online and micro-offline performance gains. Note that, the correlation distributions were significantly higher for the relationship between contextualization changes during rest and micro-offline gains than for contextualization changes during practice and either micro-online or offline gain.

With respect to the second concern highlighted above, we agree with the Reviewer that one limitation of the analysis comparing online versus offline changes in contextualization as presented in the reviewed manuscript, is that it does not eliminate the possibility that any differences could simply be explained by the passage of time (which is smaller for the online analysis compared to the offline analysis). The Reviewer suggests an approach that addresses this issue, which we have now carried out.   When quantifying online changes in contextualization from the first IndexOP1 the last IndexOP5 keypress in the same trial we observed no learning-related trend (Author response image 5, right panel). Importantly, offline distances were significantly larger than online distances regardless of the measurement approach and neither predicted online learning (Author response image 6).

Author response image 5.

Trial by trial trend of offline (left panel) and online (middle and right panels) changes in contextualization. Offline changes in contextualization were assessed by calculating the distance between neural representations for the last IndexOP5 keypress in the previous trial and the first IndexOP1 keypress in the present trial. Two different approaches were used to characterize online contextualization changes. The analysis included in the reviewed manuscript (middle panel) calculated the distance between IndexOP1 and IndexOP5 for each correct sequence, which was then averaged across the trial. This approach is limited by the lack of control for the passage of time when making online versus offline comparisons. Thus, the second approach controlled for the passage of time by calculating distance between the representations associated with the first IndexOP1 keypress and the last IndexOP5 keypress within the same trial. Note that while the first approach showed an increase online contextualization trend with practice, the second approach did not.

Author response image 6.

Relationship between online contextualization and online learning is shown for both within-sequence (left; note that this is the online contextualization measure used in the reviewd manuscript) and across-sequence (right) distance calculation. There was no significant relationship between online learning and online contextualization regardless of the measurement approach.

A related concern regarding the control analysis, where individual values for max speed and the degree of online contextualization were compared (Figure 5 Supplement 3), is whether the individual difference is meaningful. If I understood correctly, the optimization of the decoding process (temporal window, feature inclusion/reduction, decoder, etc.) was performed for individual participants, and the same feature extraction was also employed for the analysis of representation distance (i.e., contextualization). If this is the case, the distances are individually differently calculated and they may need to be normalized relative to some stable reference (e.g., 1 vs. 4 or average distance within the control sequence presses) before comparison across the individuals. 

The Reviewer makes a good point here. We have now implemented the suggested normalization procedure in the analysis provided in the revised manuscript.

Reviewer #3 (Public review): 

Summary: 

One goal of this paper is to introduce a new approach for highly accurate decoding of finger movements from human magnetoencephalography data via dimension reduction of a "multi-scale, hybrid" feature space. Following this decoding approach, the authors aim to show that early skill learning involves "contextualization" of the neural coding of individual movements, relative to their position in a sequence of consecutive movements. Furthermore, they aim to show that this "contextualization" develops primarily during short rest periods interspersed with skill training and correlates with a performance metric which the authors interpret as an indicator of offline learning. <br /> Strengths: 

A clear strength of the paper is the innovative decoding approach, which achieves impressive decoding accuracies via dimension reduction of a "multi-scale, hybrid space". This hybrid-space approach follows the neurobiologically plausible idea of the concurrent distribution of neural coding across local circuits as well as large-scale networks. A further strength of the study is the large number of tested dimension reduction techniques and classifiers (though the manuscript reveals little about the comparison of the latter). 

We appreciate the Reviewer’s comments regarding the paper’s strengths.

A simple control analysis based on shuffled class labels could lend further support to this complex decoding approach. As a control analysis that completely rules out any source of overfitting, the authors could test the decoder after shuffling class labels. Following such shuffling, decoding accuracies should drop to chance level for all decoding approaches, including the optimized decoder. This would also provide an estimate of actual chance-level performance (which is informative over and beyond the theoretical chance level). Furthermore, currently, the manuscript does not explain the huge drop in decoding accuracies for the voxel-space decoding (Figure 3B). Finally, the authors' approach to cortical parcellation raises questions regarding the information carried by varying dipole orientations within a parcel (which currently seems to be ignored?) and the implementation of the mean-flipping method (given that there are two dimensions - space and time - what do the authors refer to when they talk about the sign of the "average source", line 477?). 

The Reviewer recommends that we: 1) conduct an additional control analysis on classifier performance using shuffled class labels, 2) provide a more detailed explanation regarding the drop in decoding accuracies for the voxel-space decoding following LDA dimensionality reduction (see Fig 3B), and 3) provide additional details on how problems related to dipole solution orientations were addressed in the present study.  

In relation to the first point, we have now implemented a random shuffling approach as a control for the classification analyses. The results of this analysis indicated that the chance level accuracy was 22.12% (± SD 9.1%) for individual keypress decoding (4-class classification), and 18.41% (± SD 7.4%) for individual sequence item decoding (5-class classification), irrespective of the input feature set or the type of decoder used. Thus, the decoding accuracy observed with the final model was substantially higher than these chance levels.  

Second, please note that the dimensionality of the voxel-space feature set is very high (i.e. – 15684). LDA attempts to map the input features onto a much smaller dimensional space (number of classes-1; e.g. –  3 dimensions, for 4-class keypress decoding). Given the very high dimension of the voxel-space input features in this case, the resulting mapping exhibits reduced accuracy. Despite this general consideration, please refer to Figure 3—figure supplement 3, where we observe improvement in voxel-space decoder performance when utilizing alternative dimensionality reduction techniques.

The decoders constructed in the present study assess the average spatial patterns across time (as defined by the windowing procedure) in the input feature space.  We now provide additional details in the Methods of the revised manuscript pertaining to the parcellation procedure and how the sign ambiguity problem was addressed in our analysis.

Weaknesses: 

A clear weakness of the paper lies in the authors' conclusions regarding "contextualization". Several potential confounds, described below, question the neurobiological implications proposed by the authors and provide a simpler explanation of the results. Furthermore, the paper follows the assumption that short breaks result in offline skill learning, while recent evidence, described below, casts doubt on this assumption. 

We thank the Reviewer for giving us the opportunity to address these issues in detail (see below).

The authors interpret the ordinal position information captured by their decoding approach as a reflection of neural coding dedicated to the local context of a movement (Figure 4). One way to dissociate ordinal position information from information about the moving effectors is to train a classifier on one sequence and test the classifier on other sequences that require the same movements, but in different positions50. In the present study, however, participants trained to repeat a single sequence (4-1-3-2-4). As a result, ordinal position information is potentially confounded by the fixed finger transitions around each of the two critical positions (first and fifth press). Across consecutive correct sequences, the first keypress in a given sequence was always preceded by a movement of the index finger (=last movement of the preceding sequence), and followed by a little finger movement. The last keypress, on the other hand, was always preceded by a ring finger movement, and followed by an index finger movement (=first movement of the next sequence). Figure 4 - Supplement 2 shows that finger identity can be decoded with high accuracy (>70%) across a large time window around the time of the key press, up to at least +/-100 ms (and likely beyond, given that decoding accuracy is still high at the boundaries of the window depicted in that figure). This time window approaches the keypress transition times in this study. Given that distinct finger transitions characterized the first and fifth keypress, the classifier could thus rely on persistent (or "lingering") information from the preceding finger movement, and/or "preparatory" information about the subsequent finger movement, in order to dissociate the first and fifth keypress. Currently, the manuscript provides no evidence that the context information captured by the decoding approach is more than a by-product of temporally extended, and therefore overlapping, but independent neural representations of consecutive keypresses that are executed in close temporal proximity - rather than a neural representation dedicated to context. 

Such temporal overlap of consecutive, independent finger representations may also account for the dynamics of "ordinal coding"/"contextualization", i.e., the increase in 2-class decoding accuracy, across Day 1 (Figure 4C). As learning progresses, both tapping speed and the consistency of keypress transition times increase (Figure 1), i.e., consecutive keypresses are closer in time, and more consistently so. As a result, information related to a given keypress is increasingly overlapping in time with information related to the preceding and subsequent keypresses. The authors seem to argue that their regression analysis in Figure 5 - Figure Supplement 3 speaks against any influence of tapping speed on "ordinal coding" (even though that argument is not made explicitly in the manuscript). However, Figure 5 - Figure Supplement 3 shows inter-individual differences in a between-subject analysis (across trials, as in panel A, or separately for each trial, as in panel B), and, therefore, says little about the within-subject dynamics of "ordinal coding" across the experiment. A regression of trial-by-trial "ordinal coding" on trial-by-trial tapping speed (either within-subject or at a group-level, after averaging across subjects) could address this issue. Given the highly similar dynamics of "ordinal coding" on the one hand (Figure 4C), and tapping speed on the other hand (Figure 1B), I would expect a strong relationship between the two in the suggested within-subject (or group-level) regression. Furthermore, learning should increase the number of (consecutively) correct sequences, and, thus, the consistency of finger transitions. Therefore, the increase in 2-class decoding accuracy may simply reflect an increasing overlap in time of increasingly consistent information from consecutive keypresses, which allows the classifier to dissociate the first and fifth keypress more reliably as learning progresses, simply based on the characteristic finger transitions associated with each. In other words, given that the physical context of a given keypress changes as learning progresses - keypresses move closer together in time and are more consistently correct - it seems problematic to conclude that the mental representation of that context changes. To draw that conclusion, the physical context should remain stable (or any changes to the physical context should be controlled for). 

The issues raised by Reviewer #3 here are similar to two issues raised by Reviewer #2 above and agree they must both be carefully considered in any evaluation of our findings.

As both Reviewers pointed out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4-class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3—supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. This classification performance difference of 7.67% when tested on the Day 2 data could reflect the performance bias of the classifier for the trained sequence, possibly caused by mixed information from temporally close keypresses being incorporated into the feature weights.

Along these same lines, both Reviewers also raise the possibility that an increase in “ordinal coding/contextualization” with learning could simply reflect an increase in this mixing effect caused by faster typing speeds as opposed to an actual change in the underlying neural representation. The basic idea is that as correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged (assuming this mixing of representations is used by the classifier to differentially tag each index finger press). If this were the case, it follows that such mixing effects reflecting the ordinal sequence structure would also be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A in the previously submitted manuscript do not show this trend in the distribution of misclassifications across the four fingers.

Following this logic, it’s also possible that if the ordinal coding is largely driven by this mixing effect, the increased overlap between consecutive index finger keypresses during the 4-4 transition marking the end of one sequence and the beginning of the next one could actually mask contextualization-related changes to the underlying neural representations and make them harder to detect. In this case, a decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position might show decreased performance with learning as adjacent keypresses overlapped in time with each other to an increasing extent. However, Figure 4C in our previously submitted manuscript does not support this possibility, as the 2-class hybrid classifier displays improved classification performance over early practice trials despite greater temporal overlap.

As noted in the above replay to Reviewer #2, we also conducted a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis affirmed that the possible alternative explanation put forward by the Reviewer is not supported by our data (Adjusted R2 = 0.00431; F = 5.62). We now include this new negative control analysis result in the revised manuscript.

Finally, the Reviewer hints that one way to address this issue would be to compare MEG responses before and after learning for sequences typed at a fixed speed. However, given that the speed-accuracy trade-off should improve with learning, a comparison between unlearned and learned skill states would dictate that the skill be evaluated at a very low fixed speed. Essentially, such a design presents the problem that the post-training test is evaluating the representation in the unlearned behavioral state that is not representative of the acquired skill. Thus, this approach would not address our experimental question: “do neural representations of the same action performed at different locations within a skill sequence contextually differentiate or remain stable as learning evolves”.

A similar difference in physical context may explain why neural representation distances ("differentiation") differ between rest and practice (Figure 5). The authors define "offline differentiation" by comparing the hybrid space features of the last index finger movement of a trial (ordinal position 5) and the first index finger movement of the next trial (ordinal position 1). However, the latter is not only the first movement in the sequence but also the very first movement in that trial (at least in trials that started with a correct sequence), i.e., not preceded by any recent movement. In contrast, the last index finger of the last correct sequence in the preceding trial includes the characteristic finger transition from the fourth to the fifth movement. Thus, there is more overlapping information arising from the consistent, neighbouring keypresses for the last index finger movement, compared to the first index finger movement of the next trial. A strong difference (larger neural representation distance) between these two movements is, therefore, not surprising, given the task design, and this difference is also expected to increase with learning, given the increase in tapping speed, and the consequent stronger overlap in representations for consecutive keypresses. Furthermore, initiating a new sequence involves pre-planning, while ongoing practice relies on online planning (Ariani et al., eNeuro 2021), i.e., two mental operations that are dissociable at the level of neural representation (Ariani et al., bioRxiv 2023). 

The Reviewer argues that the comparison of last finger movement of a trial and the first in the next trial are performed in different circumstances and contexts. This is an important point and one we tend to agree with. For this task, the first sequence in a practice trial (which is pre-planned offline) is performed in a somewhat different context from the sequence iterations that follow, which involve temporally overlapping planning, execution and evaluation processes.  The Reviewer is particularly concerned about a difference in the temporal mixing effect issue raised above between the first and last keypresses performed in a trial. However, in contrast to the Reviewers stated argument above, findings from Korneysheva et. al (2019) showed that neural representations of individual actions are competitively queued during the pre-planning period in a manner that reflects the ordinal structure of the learned sequence.  Thus, mixing effects are likely still present for the first keypress in a trial. Also note that we now present new control analyses in multiple responses above confirming that hypothetical mixing effects between adjacent keypresses do not explain our reported contextualization finding. A statement addressing these possibilities raised by the Reviewer has been added to the Discussion in the revised manuscript.

In relation to pre-planning, ongoing MEG work in our lab is investigating contextualization within different time windows tailored specifically for assessing how sequence skill action planning evolves with learning.

Given these differences in the physical context and associated mental processes, it is not surprising that "offline differentiation", as defined here, is more pronounced than "online differentiation". For the latter, the authors compared movements that were better matched regarding the presence of consistent preceding and subsequent keypresses (online differentiation was defined as the mean difference between all first vs. last index finger movements during practice).  It is unclear why the authors did not follow a similar definition for "online differentiation" as for "micro-online gains" (and, indeed, a definition that is more consistent with their definition of "offline differentiation"), i.e., the difference between the first index finger movement of the first correct sequence during practice, and the last index finger of the last correct sequence. While these two movements are, again, not matched for the presence of neighbouring keypresses (see the argument above), this mismatch would at least be the same across "offline differentiation" and "online differentiation", so they would be more comparable. 

This is the same point made earlier by Reviewer #2, and we agree with this assessment. As stated in the response to Reviewer #2 above, we have now carried out quantification of online contextualization using this approach and included it in the revised manuscript. We thank the Reviewer for this suggestion.

A further complication in interpreting the results regarding "contextualization" stems from the visual feedback that participants received during the task. Each keypress generated an asterisk shown above the string on the screen, irrespective of whether the keypress was correct or incorrect. As a result, incorrect (e.g., additional, or missing) keypresses could shift the phase of the visual feedback string (of asterisks) relative to the ordinal position of the current movement in the sequence (e.g., the fifth movement in the sequence could coincide with the presentation of any asterisk in the string, from the first to the fifth). Given that more incorrect keypresses are expected at the start of the experiment, compared to later stages, the consistency in visual feedback position, relative to the ordinal position of the movement in the sequence, increased across the experiment. A better differentiation between the first and the fifth movement with learning could, therefore, simply reflect better decoding of the more consistent visual feedback, based either on the feedback-induced brain response, or feedback-induced eye movements (the study did not include eye tracking). It is not clear why the authors introduced this complicated visual feedback in their task, besides consistency with their previous studies.

We strongly agree with the Reviewer that eye movements related to task engagement are important to rule out as a potential driver of the decoding accuracy or contextualization effect. We address this issue above in response to a question raised by Reviewer #1 about the impact of movement related artefacts in general on our findings.

First, the assumption the Reviewer makes here about the distribution of errors in this task is incorrect. On average across subjects, 2.32% ± 1.48% (mean ± SD) of all keypresses performed were errors, which were evenly distributed across the four possible keypress responses. While errors increased progressively over practice trials, they did so in proportion to the increase in correct keypresses, so that the overall ratio of correct-to-incorrect keypresses remained stable over the training session. Thus, the Reviewer’s assumptions that there is a higher relative frequency of errors in early trials, and a resulting systematic trend phase shift differences between the visual display updates (i.e. – a change in asterisk position above the displayed sequence) and the keypress performed is not substantiated by the data. To the contrary, the asterisk position on the display and the keypress being executed remained highly correlated over the entire training session. We now include a statement about the frequency and distribution of errors in the revised manuscript.

Given this high correlation, we firmly agree with the Reviewer that the issue of eye movement-related artefacts is still an important one to address. Fortunately, we did collect eye movement data during the MEG recordings so were able to investigate this. As detailed in the response to Reviewer #1 above, we found that gaze positions and eye-movement velocity time-locked to visual display updates (i.e. – a change in asterisk position above the displayed sequence) did not reflect the asterisk location above chance levels (Overall cross-validated accuracy = 0.21817; see Author response image 1). Furthermore, an inspection of the eye position data revealed that a majority of participants on most trials displayed random walk gaze patterns around a center fixation point, indicating that participants did not attend to the asterisk position on the display. This is consistent with intrinsic generation of the action sequence, and congruent with the fact that the display does not provide explicit feedback related to performance. As pointed out above, a similar real-world example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks), which is typically ignored by the user. Notably, the minimal participant engagement with the visual task display observed in this study highlights an important difference between behavior observed during explicit sequence learning motor tasks (which is highly generative in nature) with reactive responses to stimulus cues in a serial reaction time task (SRTT).  This is a crucial difference that must be carefully considered when comparing findings across studies. All elements pertaining to this new control analysis are now included in the revised manuscript.

The authors report a significant correlation between "offline differentiation" and cumulative micro-offline gains. However, it would be more informative to correlate trial-by-trial changes in each of the two variables. This would address the question of whether there is a trial-by-trial relation between the degree of "contextualization" and the amount of micro-offline gains - are performance changes (micro-offline gains) less pronounced across rest periods for which the change in "contextualization" is relatively low? Furthermore, is the relationship between micro-offline gains and "offline differentiation" significantly stronger than the relationship between micro-offline gains and "online differentiation"? 

In response to a similar issue raised above by Reviewer #2, we now include new analyses comparing correlation magnitudes between (1) “online differention” vs micro-online gains, (2) “online differention” vs micro-offline gains and (3) “offline differentiation” and micro-offline gains (see Author response images 4, 5 and 6 above). These new analyses and results have been added to the revised manuscript. Once again, we thank both Reviewers for this suggestion.

The authors follow the assumption that micro-offline gains reflect offline learning.

This statement is incorrect. The original Bonstrup et al (2019) 49 paper clearly states that micro-offline gains must be carefully interpreted based upon the behavioral context within which they are observed, and lays out the conditions under which one can have confidence that micro-offline gains reflect offline learning.  In fact, the excellent meta-analysis of Pan & Rickard (2015) 51, which re-interprets the benefits of sleep in overnight skill consolidation from a “reactive inhibition” perspective, was a crucial resource in the experimental design of our initial study49, as well as in all our subsequent work. Pan & Rickard stated:

“Empirically, reactive inhibition refers to performance worsening that can accumulate during a period of continuous training (Hull, 1943). It tends to dissipate, at least in part, when brief breaks are inserted between blocks of training. If there are multiple performance-break cycles over a training session, as in the motor sequence literature, performance can exhibit a scalloped effect, worsening during each uninterrupted performance block but improving across blocks52,53. Rickard, Cai, Rieth, Jones, and Ard (2008) and Brawn, Fenn, Nusbaum, and Margoliash (2010) 52,53 demonstrated highly robust scalloped reactive inhibition effects using the commonly employed 30 s–30 s performance break cycle, as shown for Rickard et al.’s (2008) massed practice sleep group in Figure 2. The scalloped effect is evident for that group after the first few 30 s blocks of each session. The absence of the scalloped effect during the first few blocks of training in the massed group suggests that rapid learning during that period masks any reactive inhibition effect.”

Crucially, Pan & Rickard51 made several concrete recommendations for reducing the impact of the reactive inhibition confound on offline learning studies. One of these recommendations was to reduce practice times to 10s (most prior sequence learning studies up until that point had employed 30s long practice trials). They stated:

“The traditional design involving 30 s-30 s performance break cycles should be abandoned given the evidence that it results in a reactive inhibition confound, and alternative designs with reduced performance duration per block used instead 51. One promising possibility is to switch to 10 s performance durations for each performance-break cycle Instead 51. That design appears sufficient to eliminate at least the majority of the reactive inhibition effect 52,53.”

We mindfully incorporated recommendations from Pan and Rickard51  into our own study designs including 1) utilizing 10s practice trials and 2) constraining our analysis of micro-offline gains to early learning trials (where performance monotonically increases and 95% of overall performance gains occur), which are prior to the emergence of the “scalloped” performance dynamics that are strongly linked to reactive inhibition effects. 

However, there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.

We strongly disagree with the Reviewer’s assertion that “there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.”  The initial Bönstrup et al. (2019) 49 report was followed up by a large online crowd-sourcing study (Bönstrup et al., 2020) 54. This second (and much larger) study provided several additional important findings supporting our interpretation of micro-offline gains in cases where the important behavioral conditions clarified above were met (see Author response image 7 below for further details on these conditions).

Author response image 7.

Micro-offline gains observed in learning and non-learning contexts are attributed to different underlying causes. (A) Micro-offline and online changes relative to overall trial-by-trial learning. This figure is based on data from Bönstrup et al. (2019) 49. During early learning, micro-offline gains (red bars) closely track trial-by-trial performance gains (green line with open circle markers), with minimal contribution from micro-online gains (blue bars). The stated conclusion in Bönstrup et al. (2019) is that micro-offline gains only during this Early Learning stage reflect rapid memory consolidation (see also 54). After early learning, about practice trial 11, skill plateaus. This plateau skill period is characterized by a striking emergence of coupled (and relatively stable) micro-online drops and micro-offline increases. Bönstrup et al. (2019) as well as others in the literature 55-57, argue that micro-offline gains during the plateau period likely reflect recovery from inhibitory performance factors such as reactive inhibition or fatigue, and thus must be excluded from analyses relating micro-offline gains to skill learning.  The Non-repeating groups in Experiments 3 and 4 from Das et al. (2024) suffer from a lack of consideration of these known confounds.

Evidence documented in that paper54 showed that micro-offline gains during early skill learning were: 1) replicable and generalized to subjects learning the task in their daily living environment (n=389); 2) equivalent when significantly shortening practice period duration, thus confirming that they are not a result of recovery from performance fatigue (n=118);  3) reduced (along with learning rates) by retroactive interference applied immediately after each practice period relative to interference applied after passage of time (n=373), indicating stabilization of the motor memory at a microscale of several seconds consistent with rapid consolidation; and 4) not modified by random termination of the practice periods, ruling out a contribution of predictive motor slowing (N = 71) 54.  Altogether, our findings were strongly consistent with the interpretation that micro-offline gains reflect memory consolidation supporting early skill learning. This is precisely the portion of the learning curve Pan and Rickard51 refer to when they state “…rapid learning during that period masks any reactive inhibition effect”.

This interpretation is further supported by brain imaging evidence linking known memory-related networks and consolidation mechanisms to micro-offline gains. First, we reported that the density of fast hippocampo-neocortical skill memory replay events increases approximately three-fold during early learning inter-practice rest periods with the density explaining differences in the magnitude of micro-offline gains across subjects1. Second, Jacobacci et al. (2020) independently reproduced our original behavioral findings and reported BOLD fMRI changes in the hippocampus and precuneus (regions also identified in our MEG study1) linked to micro-offline gains during early skill learning. 33 These functional changes were coupled with rapid alterations in brain microstructure in the order of minutes, suggesting that the same network that operates during rest periods of early learning undergoes structural plasticity over several minutes following practice58. Third, even more recently, Chen et al. (2024) provided direct evidence from intracranial EEG in humans linking sharp-wave ripple events (which are known markers for neural replay59) in the hippocampus (80-120 Hz in humans) with micro-offline gains during early skill learning. The authors report that the strong increase in ripple rates tracked learning behavior, both across blocks and across participants. The authors conclude that hippocampal ripples during resting offline periods contribute to motor sequence learning. 2

Thus, there is actually now substantial evidence in the literature directly supporting the assertion “that micro-offline gains really result from offline learning”.  On the contrary, according to Gupta & Rickard (2024) “…the mechanism underlying RI [reactive inhibition] is not well established” after over 80 years of investigation60, possibly due to the fact that “reactive inhibition” is a categorical description of behavioral effects that likely result from several heterogenous processes with very different underlying mechanisms.

On the contrary, recent evidence questions this interpretation (Gupta & Rickard, npj Sci Learn 2022; Gupta & Rickard, Sci Rep 2024; Das et al., bioRxiv 2024). Instead, there is evidence that micro-offline gains are transient performance benefits that emerge when participants train with breaks, compared to participants who train without breaks, however, these benefits vanish within seconds after training if both groups of participants perform under comparable conditions (Das et al., bioRxiv 2024). 

It is important to point out that the recent work of Gupta & Rickard (2022,2024) 55 does not present any data that directly opposes our finding that early skill learning49 is expressed as micro-offline gains during rest breaks. These studies are essentially an extension of the Rickard et al (2008) paper that employed a massed (30s practice followed by 30s breaks) vs spaced (10s practice followed by 10s breaks) to assess if recovery from reactive inhibition effects could account for performance gains measured after several minutes or hours. Gupta & Rickard (2022) added two additional groups (30s practice/10s break and 10s practice/10s break as used in the work from our group). The primary aim of the study was to assess whether it was more likely that changes in performance when retested 5 minutes after skill training (consisting of 12 practice trials for the massed groups and 36 practice trials for the spaced groups) had ended reflected memory consolidation effects or recovery from reactive inhibition effects. The Gupta & Rickard (2024) follow-up paper employed a similar design with the primary difference being that participants performed a fixed number of sequences on each trial as opposed to trials lasting a fixed duration. This was done to facilitate the fitting of a quantitative statistical model to the data.  To reiterate, neither study included any analysis of micro-online or micro-offline gains and did not include any comparison focused on skill gains during early learning. Instead, Gupta & Rickard (2022), reported evidence for reactive inhibition effects for all groups over much longer training periods. Again, we reported the same finding for trials following the early learning period in our original Bönstrup et al. (2019) paper49 (Author response image 7). Also, please note that we reported in this paper that cumulative micro-offline gains over early learning did not correlate with overnight offline consolidation measured 24 hours later49 (see the Results section and further elaboration in the Discussion). Thus, while the composition of our data is supportive of a short-term memory consolidation process operating over several seconds during early learning, it likely differs from those involved over longer training times and offline periods, as assessed by Gupta & Rickard (2022).

In the recent preprint from Das et al (2024) 61,  the authors make the strong claim that “micro-offline gains during early learning do not reflect offline learning” which is not supported by their own data.   The authors hypothesize that if “micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”.  The study utilizes a spaced vs. massed practice group between-subjects design inspired by the reactive inhibition work from Rickard and others to test this hypothesis. Crucially, the design incorporates only a small fraction of the training used in other investigations to evaluate early skill learning1,33,49,54,57,58,62.  A direct comparison between the practice schedule designs for the spaced and massed groups in Das et al., and the training schedule all participants experienced in the original Bönstrup et al. (2019) paper highlights this issue as well as several others (Author response image 8):

Author response image 8.

(A) Comparison of Das et al. Spaced & Massed group training session designs, and the training session design from the original Bönstrup et al. (2019) 49 paper. Similar to the approach taken by Das et al., all practice is visualized as 10-second practice trials with a variable number (either 0, 1 or 30) of 10-second-long inter-practice rest intervals to allow for direct comparisons between designs. The two key takeaways from this comparison are that (1) the intervention differences (i.e. – practice schedules) between the Massed and Spaced groups from the Das et al. report are extremely small (less than 12% of the overall session schedule) and (2) the overall amount of practice is much less than compared to the design from the original Bönstrup report 49  (which has been utilized in several subsequent studies). (B) Group-level learning curve data from Bönstrup et al. (2019) 49 is used to estimate the performance range accounted for by the equivalent periods covering Test 1, Training 1 and Test 2 from Das et al (2024). Note that the intervention in the Das et al. study is limited to a period covering less than 50% of the overall learning range.

First, participants in the original Bönstrup et al. study 49 experienced 157.14% more practice time and 46.97% less inter-practice rest time than the Spaced group in the Das et al. study (Author response image 8).  Thus, the overall amount of practice and rest differ substantially between studies, with much more limited training occurring for participants in Das et al.  

Second, and perhaps most importantly, the actual intervention (i.e. – the difference in practice schedule between the Spaced and Massed groups) employed by Das et al. covers a very small fraction of the overall training session. Identical practice schedule segments for both the Spaced & Massed groups are indicated by the red shaded area in Author response image 8. Please note that these identical segments cover 94.84% of the Massed group training schedule and 88.01% of the Spaced group training schedule (since it has 60 seconds of additional rest). This means that the actual interventions cover less than 5% (for Massed) and 12% (for Spaced) of the total training session, which minimizes any chance of observing a difference between groups.

Also note that the very beginning of the practice schedule (during which Figure R9 shows substantial learning is known to occur) is labeled in the Das et al. study as Test 1.  Test 1 encompasses the first 20 seconds of practice (alternatively viewed as the first two 10-second-long practice trials with no inter-practice rest). This is immediately followed by the Training 1 intervention, which is composed of only three 10-second-long practice trials (with 10-second inter-practice rest for the Spaced group and no inter-practice rest for the Massed group). Author response image 8 also shows that since there is no inter-practice rest after the third Training practice trial for the Spaced group, this third trial (for both Training 1 and 2) is actually a part of an identical practice schedule segment shared by both groups (Massed and Spaced), reducing the magnitude of the intervention even further.

Moreover, we know from the original Bönstrup et al. (2019) paper49 that 46.57% of all overall group-level performance gains occurred between trials 2 and 5 for that study. Thus, Das et al. are limiting their designed intervention to a period covering less than half of the early learning range discussed in the literature, which again, minimizes any chance of observing an effect.

This issue is amplified even further at Training 2 since skill learning prior to the long 5-minute break is retained, further constraining the performance range over these three trials. A related issue pertains to the trials labeled as Test 1 (trials 1-2) and Test 2 (trials 6-7) by Das et al. Again, we know from the original Bönstrup et al. paper 49 that 18.06% and 14.43% (32.49% total) of all overall group-level performance gains occurred during trials corresponding to Das et al Test 1 and Test 2, respectively. In other words, Das et al averaged skill performance over 20 seconds of practice at two time-points where dramatic skill improvements occur. Pan & Rickard (1995) previously showed that such averaging is known to inject artefacts into analyses of performance gains.

Furthermore, the structure of the Test in Das et. al study appears to have an interference effect on the Spaced group performance after the training intervention.  This makes sense if you consider that the Spaced group is required to now perform the task in a Massed practice environment (i.e., two 10-second-long practice trials merged into one long trial), further blurring the true intervention effects. This effect is observable in Figure 1C,E of their pre-print. Specifically, while the Massed group continues to show an increase in performance during test relative to the last 10 seconds of practice during training, the Spaced group displays a marked decrease. This decrease is in stark contrast to the monotonic increases observed for both groups at all other time-points.

Interestingly, when statistical comparisons between the groups are made at the time-points when the intervention is present (as opposed to after it has been removed) then the stated hypothesis, “If micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”, is confirmed.

The data presented by Gupta and Rickard (2022, 2024) and Das et al. (2024) is in many ways more confirmatory of the constraints employed by our group and others with respect to experimental design, analysis and interpretation of study findings, rather than contradictory. Still, it does highlight a limitation of the current micro-online/offline framework, which was originally only intended to be applied to early skill learning over spaced practice schedules when reactive inhibition effects are minimized49. Extrapolation of this current framework to post-plateau performance periods, longer timespans, or non-learning situations (e.g. – the Non-repeating groups from Experiments 3 & 4 in Das et al. (2024)), when reactive inhibition plays a more substantive role, is not warranted. Ultimately, it will be important to develop new paradigms allowing one to independently estimate the different coincident or antagonistic features (e.g. - memory consolidation, planning, working memory and reactive inhibition) contributing to micro-online and micro-offline gains during and after early skill learning within a unifying framework.

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Author response:

eLife assessment

This potentially useful study involves neuro-imaging and electrophysiology in a small cohort of congenital cataract patients after sight recovery and age-matched control participants with normal sight. It aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in the visual cortex. While the findings are taken to suggest the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, the evidence supporting these claims is incomplete. Specifically, small sample sizes, lack of a specific control cohort, and other methodological limitations will likely restrict the usefulness of the work, with relevance limited to scientists working in this particular subfield.

As pointed out in the public reviews, there are only very few human models which allow for assessing the role of early experience on neural circuit development. While the prevalent research in permanent congenital blindness reveals the response and adaptation of the developing brain to an atypical situation (blindness), research in sight restoration addresses the question of whether and how atypical development can be remediated if typical experience (vision) is restored. The literature on the role of visual experience in the development of E/I balance in humans, assessed via Magnetic Resonance Spectroscopy (MRS), has been limited to a few studies on congenital permanent blindness. Thus, we assessed sight recovery individuals with a history of congenital blindness, as limited evidence from other researchers indicated that the visual cortex E/I ratio might differ compared to normally sighted controls.

Individuals with total bilateral congenital cataracts who remained untreated until later in life are extremely rare, particularly if only carefully diagnosed patients are included in a study sample. A sample size of 10 patients is, at the very least, typical of past studies in this population, even for exclusively behavioral assessments. In the present study, in addition to behavioral assessment as an indirect measure of sensitive periods, we investigated participants with two neuroimaging methods (Magnetic Resonance Spectroscopy and electroencephalography) to directly assess the neural correlates of sensitive periods in humans. The electroencephalography data allowed us to link the results of our small sample to findings documented in large cohorts of both, sight recovery individuals and permanently congenitally blind individuals. As pointed out in a recent editorial recommending an “exploration-then-estimation procedure,” (“Consideration of Sample Size in Neuroscience Studies,” 2020), exploratory studies like ours provide crucial direction and specific hypotheses for future work.

We included an age-matched sighted control group recruited from the same community, measured in the same scanner and laboratory, to assess whether early experience is necessary for a typical excitatory/inhibitory (E/I) ratio to emerge in adulthood. The present findings indicate that this is indeed the case. Based on these results, a possible question to answer in future work, with individuals who had developmental cataracts, is whether later visual deprivation causes similar effects. Note that even if visual deprivation at a later stage in life caused similar effects, the current results would not be invalidated; by contrast, they are essential to understand future work on late (permanent or transient) blindness.

Thus, we think that the present manuscript has far reaching implications for our understanding of the conditions under which E/I balance, a crucial characteristic of brain functioning, emerges in humans.

Finally, our manuscript is one of the first few studies which relates MRS neurotransmitter concentrations to parameters of EEG aperiodic activity. Since present research has been using aperiodic activity as a correlate of the E/I ratio, and partially of higher cognitive functions, we think that our manuscript additionally contributes to a better understanding of what might be measured with aperiodic neurophysiological activity.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this human neuroimaging and electrophysiology study, the authors aimed to characterize the effects of a period of visual deprivation in the sensitive period on excitatory and inhibitory balance in the visual cortex. They attempted to do so by comparing neurochemistry conditions ('eyes open', 'eyes closed') and resting state, and visually evoked EEG activity between ten congenital cataract patients with recovered sight (CC), and ten age-matched control participants (SC) with normal sight.

First, they used magnetic resonance spectroscopy to measure in vivo neurochemistry from two locations, the primary location of interest in the visual cortex, and a control location in the frontal cortex. Such voxels are used to provide a control for the spatial specificity of any effects because the single-voxel MRS method provides a single sampling location. Using MR-visible proxies of excitatory and inhibitory neurotransmission, Glx and GABA+ respectively, the authors report no group effects in GABA+ or Glx, no difference in the functional conditions 'eyes closed' and 'eyes open'. They found an effect of the group in the ratio of Glx/GABA+ and no similar effect in the control voxel location. They then performed multiple exploratory correlations between MRS measures and visual acuity, and reported a weak positive correlation between the 'eyes open' condition and visual acuity in CC participants.

The same participants then took part in an EEG experiment. The authors selected only two electrodes placed in the visual cortex for analysis and reported a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

The authors report the difference in E/I ratio, and interpret the lower E/I ratio as representing an adaptation to visual deprivation, which would have initially caused a higher E/I ratio. Although intriguing, the strength of evidence in support of this view is not strong. Amongst the limitations are the low sample size, a critical control cohort that could provide evidence for a higher E/I ratio in CC patients without recovered sight for example, and lower data quality in the control voxel.

Strengths of study:

How sensitive period experience shapes the developing brain is an enduring and important question in neuroscience. This question has been particularly difficult to investigate in humans. The authors recruited a small number of sight-recovered participants with bilateral congenital cataracts to investigate the effect of sensitive period deprivation on the balance of excitation and inhibition in the visual brain using measures of brain chemistry and brain electrophysiology. The research is novel, and the paper was interesting and well-written.

Limitations:

(1.1) Low sample size. Ten for CC and ten for SC, and a further two SC participants were rejected due to a lack of frontal control voxel data. The sample size limits the statistical power of the dataset and increases the likelihood of effect inflation.

Applying strict criteria, we only included individuals who were born with no patterned vision in the CC group. The population of individuals who have remained untreated past infancy is small in India, despite a higher prevalence of childhood cataract than Germany. Indeed, from the original 11 CC and 11 SC participants tested, one participant each from the CC and SC group had to be rejected, as their data had been corrupted, resulting in 10 participants in each group.

It was a challenge to recruit participants from this rare group with no history of neurological diagnosis/intake of neuromodulatory medications, who were able and willing to undergo both MRS and EEG. For this study, data collection took more than 1.5 years.

We took care of the validity of our results with two measures; first, assessed not just MRS, but additionally, EEG measures of E/I ratio. The latter allowed us to link results to a larger population of CC individuals, that is, we replicated the results of a larger group of 38 individuals (Ossandón et al., 2023) in our sub-group.

Second, we included a control voxel. As predicted, all group effects were restricted to the occipital voxel.

(1.2) Lack of specific control cohort. The control cohort has normal vision. The control cohort is not specific enough to distinguish between people with sight loss due to different causes and patients with congenital cataracts with co-morbidities. Further data from more specific populations, such as patients whose cataracts have not been removed, with developmental cataracts, or congenitally blind participants, would greatly improve the interpretability of the main finding. The lack of a more specific control cohort is a major caveat that limits a conclusive interpretation of the results.

The existing work on visual deprivation and neurochemical changes, as assessed with MRS, has been limited to permanent congenital blindness. In fact, most of the studies on permanent blindness included only congenitally blind or early blind humans (Coullon et al., 2015; Weaver et al., 2013), or, in separate studies, only late-blind individuals (Bernabeu et al., 2009). Thus, accordingly, we started with the most “extreme” visual deprivation model, sight recovery after congenital blindness. If we had not observed any group difference compared to normally sighted controls, investigating other groups might have been trivial. Based on our results, subsequent studies in late blind individuals, and then individuals with developmental cataracts, can be planned with clear hypotheses.

(1.3) MRS data quality differences. Data quality in the control voxel appears worse than in the visual cortex voxel. The frontal cortex MRS spectrum shows far broader linewidth than the visual cortex (Supplementary Figures). Compared to the visual voxel, the frontal cortex voxel has less defined Glx and GABA+ peaks; lower GABA+ and Glx concentrations, lower NAA SNR values; lower NAA concentrations. If the data quality is a lot worse in the FC, then small effects may not be detectable.

Worse data quality in the frontal than the visual cortex has been repeatedly observed in the MRS literature, attributable to magnetic field distortions (Juchem & Graaf, 2017) resulting from the proximity of the region to the sinuses (recent example: (Rideaux et al., 2022)). Nevertheless, we chose the frontal control region rather than a parietal voxel, given the potential  neurochemical changes in multisensory regions of the parietal cortex due to blindness. Such reorganization would be less likely in frontal areas associated with higher cognitive functions. Further, prior MRS studies of the visual cortex have used the frontal cortex as a control region as well (Pitchaimuthu et al., 2017; Rideaux et al., 2022).

In the present study, we checked that the frontal cortex datasets for Glx and GABA+ concentrations were of sufficient quality: the fit error was below 8.31% in both groups (Supplementary Material S3). For reference, Mikkelsen et al. reported a mean GABA+ fit error of 6.24 +/- 1.95% from a posterior cingulate cortex voxel across 8 GE scanners, using the Gannet pipeline. No absolute cutoffs have been proposed for fit errors. However, MRS studies in special populations (I/E ratio assessed in narcolepsy (Gao et al., 2024), GABA concentration assessed in Autism Spectrum Disorder (Maier et al., 2022)) have used frontal cortex data with a fit error of <10% to identify differences between cohorts (Gao et al., 2024; Pitchaimuthu et al., 2017). Based on the literature, MRS data from the frontal voxel of the present study would have been of sufficient quality to uncover group differences.

In the revised manuscript, we will add the recently published MRS quality assessment form to the supplementary materials. Additionally, we would like to allude to our apriori prediction of group differences for the visual cortex, but not for the frontal cortex voxel.

(1.4) Because of the direction of the difference in E/I, the authors interpret their findings as representing signatures of sight improvement after surgery without further evidence, either within the study or from the literature. However, the literature suggests that plasticity and visual deprivation drive the E/I index up rather than down. Decreasing GABA+ is thought to facilitate experience-dependent remodelling. What evidence is there that cortical inhibition increases in response to a visual cortex that is over-sensitised due to congenital cataracts? Without further experimental or literature support this interpretation remains very speculative.

Indeed, higher inhibition was not predicted, which we attempt to reconcile in our discussion section. We base our discussion mainly on the non-human animal literature, which has shown evidence of homeostatic changes after prolonged visual deprivation in the adult brain (Barnes et al., 2015). It is also interesting to note that after monocular deprivation in adult humans, resting GABA+ levels decreased in the visual cortex (Lunghi et al., 2015). Assuming that after delayed sight restoration, adult neuroplasticity mechanisms must be employed, these studies would predict a “balancing” of the increased excitatory drive following sight restoration by a commensurate increase in inhibition (Keck et al., 2017). Additionally, the EEG results of the present study allowed for speculation regarding the underlying neural mechanisms of an altered E/I ratio. The aperiodic EEG activity suggested higher spontaneous spiking (increased intercept) and increased inhibition (steeper aperiodic slope between 1-20 Hz) in CC vs SC individuals (Ossandón et al., 2023).

In the revised manuscript, we will more clearly indicate that these speculations are based primarily on non-human animal work, due to the lack of human studies on the subject.

(1.5) Heterogeneity in the patient group. Congenital cataract (CC) patients experienced a variety of duration of visual impairment and were of different ages. They presented with co-morbidities (absorbed lens, strabismus, nystagmus). Strabismus has been associated with abnormalities in GABAergic inhibition in the visual cortex. The possible interactions with residual vision and confounds of co-morbidities are not experimentally controlled for in the correlations, and not discussed.

The goal of the present study was to assess whether we would observe changes in E/I ratio after restoring vision at all. We would not have included patients without nystagmus in the CC group of the present study, since it would have been unlikely that they experienced congenital patterned visual deprivation. Amongst diagnosticians, nystagmus or strabismus might not be considered genuine “comorbidities” that emerge in people with congenital cataracts. Rather, these are consequences of congenital visual deprivation, which we employed as diagnostic criteria. Similarly, absorbed lenses are clear signs that cataracts were congenital. As in other models of experience dependent brain development (e.g. the extant literature on congenital permanent blindness, including anophthalmic individuals (Coullon et al., 2015; Weaver et al., 2013), some uncertainty remains regarding whether the (remaining, in our case) abnormalities of the eye, or the blindness they caused, are the factors driving neural changes. In case of people with reversed congenital cataracts, at least the retina is considered to be intact, as they would otherwise not receive cataract removal surgery.

However, we consider it unlikely that strabismus caused the group differences, because the present study shows group differences in the Glx/GABA+ ratio at rest, regardless of eye opening or eye closure, for which strabismus would have caused distinct effects. By contrast, the link between GABA concentration and, for example, interocular suppression in strabismus, have so far been documented during visual stimulation (Mukerji et al., 2022; Sengpiel et al., 2006), and differed in direction depending on the amblyopic vs. non-amblyopic eye. Further, one MRS study did not find group differences in GABA concentration between the visual cortices of 16 amblyopic individuals and sighted controls (Mukerji et al., 2022), supporting that the differences in Glx/GABA+ concentration which we observed were driven by congenital deprivation, and not amblyopia-associated visual acuity or eye movement differences.  

In the revised manuscript, we will discuss the inclusion criteria in more detail, and the aforementioned reasons why our data remains interpretable.

(1.6) Multiple exploratory correlations were performed to relate MRS measures to visual acuity (shown in Supplementary Materials), and only specific ones were shown in the main document. The authors describe the analysis as exploratory in the 'Methods' section. Furthermore, the correlation between visual acuity and E/I metric is weak, and not corrected for multiple comparisons. The results should be presented as preliminary, as no strong conclusions can be made from them. They can provide a hypothesis to test in a future study.

In the revised manuscript, we will clearly indicate that the exploratory correlation analyses are reported to put forth hypotheses for future studies.

(1.7) P.16 Given the correlation of the aperiodic intercept with age ("Age negatively correlated with the aperiodic intercept across CC and SC individuals, that is, a flattening of the intercept was observed with age"), age needs to be controlled for in the correlation between neurochemistry and the aperiodic intercept. Glx has also been shown to negatively correlate with age.

The correlation between chronological age and aperiodic intercept was observed across groups, but the correlation between Glx and the intercept of the aperiodic EEG activity was seen only in the CC group, even though the SC group was matched for age. Thus, such a correlation was very unlikely to  be predominantly driven by an effect of chronological age.

In the revised manuscript, we will add the linear regressions with age as a covariate included below, for the relationship between aperiodic intercept and Glx concentration in the CC group. 

a. A linear regression was conducted within the CC group to predict the intercept during visual stimulation, based on age and visual cortex Glx concentration. The results of the regression analysis indicated that the model explained a significant proportion of the variance in the aperiodic intercept, 𝑅2\=0.82_, t_(2,7)=16.1_, 𝑝=0.0024._ Note that the coefficient for age was not significant, 𝛽=0.007, t(7)=0.82, 𝑝=0.439. The regression coefficients and their respective statistics are presented in Author response table 1.

Author response table 1.

Regression Analysis Summary for Predicting Aperiodic Intercept (Visual Stimulation) in the CC group

b. A linear regression was conducted to predict the intercept during eye opening at rest, based on age and visual cortex Glx concentration. The results of the regression analysis indicated that the model explained a significant proportion of the variance in the aperiodic intercept, 𝑅2\=0.842_, t_(2,7)=18.6,  𝑝=0.00159_._ Note that the coefficient for age was not significant, 𝛽=−0.005, t(7)=−0.90, 𝑝=0.400. The regression coefficients and their respective statistics are presented in Author response table 2.

Author response table 2.

Regression Analysis Summary for Predicting Aperiodic Intercept (Eyes Open) in the CC group

c. Given that the Glx coefficient is significant in both models and age does not significantly predict either outcome, it can be concluded that Glx independently predicts the intercept of the aperiodic intercept.

(1.8) Multiple exploratory correlations were performed to relate MRS to EEG measures (shown in Supplementary Materials), and only specific ones were shown in the main document. Given the multiple measures from the MRS, the correlations with the EEG measures were exploratory, as stated in the text, p.16, and in Figure 4. Yet the introduction said that there was a prior hypothesis "We further hypothesized that neurotransmitter changes would relate to changes in the slope and intercept of the EEG aperiodic activity in the same subjects." It would be great if the text could be revised for consistency and the analysis described as exploratory.

In the revised manuscript, we will improve the phrasing. We consider the correlation analyses as exploratory due to our sample size and the absence of prior work. However, we did hypothesize that both MRS and EEG markers would concurrently be altered in CC vs SC individuals.

(1.9) The analysis for the EEG needs to take more advantage of the available data. As far as I understand, only two electrodes were used, yet far more were available as seen in their previous study (Ossandon et al., 2023). The spatial specificity is not established. The authors could use the frontal cortex electrode (FP1, FP2) signals as a control for spatial specificity in the group effects, or even better, all available electrodes and correct for multiple comparisons. Furthermore, they could use the aperiodic intercept vs Glx in SC to evaluate the specificity of the correlation to CC.

The aperiodic intercept and slope did not differ between CC and SC individuals for Fp1 and Fp2, suggesting the spatial specificity of the results. In the revised manuscript, we will add this analysis to the supplementary material.

Author response image 1.

Aperiodic intercept (top) and slope (bottom) for congenital cataract-reversal (CC, red) and age-matched normally sighted control (SC, blue) individuals. Distributions of these parameters are displayed as violin plots for three conditions; at rest with eyes closed (EC), at rest with eyes open (EO) and during visual stimulation (LU). Aperiodic parameters were calculated across electrodes Fp1 and Fp2. Solid black lines indicate mean values, dotted black lines indicate median values. Coloured lines connect values of individual participants across conditions.

Further, Glx concentration in the visual cortex did not correlate with the aperiodic intercept in the SC group (Figure 4), suggesting that this relationship was indeed specific to the CC group.

The data from all electrodes has been analyzed and published in other studies as well (Pant et al., 2023; Ossandón et al., 2023).

Reviewer #2 (Public Review):

Summary:

The manuscript reports non-invasive measures of activity and neurochemical profiles of the visual cortex in congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts. The declared aim of the study is to find out how restoring visual function after several months or years of complete blindness impacts the balance between excitation and inhibition in the visual cortex.

Strengths:

The findings are undoubtedly useful for the community, as they contribute towards characterising the many ways this special population differs from normally sighted individuals. The combination of MRS and EEG measures is a promising strategy to estimate a fundamental physiological parameter - the balance between excitation and inhibition in the visual cortex, which animal studies show to be heavily dependent upon early visual experience. Thus, the reported results pave the way for further studies, which may use a similar approach to evaluate more patients and control groups.

Weaknesses:

(2.1) The main issue is the lack of an appropriate comparison group or condition to delineate the effect of sight recovery (as opposed to the effect of congenital blindness). Few previous studies suggested an increased excitation/Inhibition ratio in the visual cortex of congenitally blind patients; the present study reports a decreased E/I ratio instead. The authors claim that this implies a change of E/I ratio following sight recovery. However, supporting this claim would require showing a shift of E/I after vs. before the sight-recovery surgery, or at least it would require comparing patients who did and did not undergo the sight-recovery surgery (as common in the field).

Longitudinal studies would indeed be the best way to test the hypothesis that the lower E/I ratio in the CC group observed by the present study is a consequence of sight restoration. However, longitudinal studies involving neuroimaging are an effortful challenge, particularly in research conducted outside of major developed countries and dedicated neuroimaging research facilities. Crucially, however, had CC and SC individuals, as well as permanently congenitally blind vs SC individuals (Coullon et al., 2015; Weaver et al., 2013), not differed on any neurochemical markers, such a longitudinal study might have been trivial. Thus, in order to justify and better tailor longitudinal studies, cross-sectional studies are an initial step.

(2.2) MR Spectroscopy shows a reduced GLX/GABA ratio in patients vs. sighted controls; however, this finding remains rather isolated, not corroborated by other observations. The difference between patients and controls only emerges for the GLX/GABA ratio, but there is no accompanying difference in either the GLX or the GABA concentrations. There is an attempt to relate the MRS data with acuity measurements and electrophysiological indices, but the explorative correlational analyses do not help to build a coherent picture. A bland correlation between GLX/GABA and visual impairment is reported, but this is specific to the patients' group (N=10) and would not hold across groups (the correlation is positive, predicting the lowest GLX/GABA ratio values for the sighted controls - the opposite of what is found). There is also a strong correlation between GLX concentrations and the EEG power at the lowest temporal frequencies. Although this relation is intriguing, it only holds for a very specific combination of parameters (of the many tested): only with eyes open, only in the patient group.

We interpret these findings differently, that is, in the context of experiments from non-human animals and the larger MRS literature.

Homeostatic control of E/I balance assumes that the ratio of excitation (reflected here by Glx) and inhibition (reflected here by GABA+) is regulated. Like prior work (Gao et al., 2024, 2024; Narayan et al., 2022; Perica et al., 2022; Steel et al., 2020; Takado et al., 2022; Takei et al., 2016), we assumed that the ratio of Glx/GABA+ is indicative of E/I balance rather than solely the individual neurotransmitter levels. One of the motivations for assessing the ratio vs the absolute concentration is that as per the underlying E/I balance hypothesis, a change in excitation would cause a concomitant change in inhibition, and vice versa, which has been shown in non-human animal work (Fang et al., 2021; Haider et al., 2006; Tao & Poo, 2005) and modeling research (Vreeswijk & Sompolinsky, 1996; Wu et al., 2022). Importantly, our interpretation of the lower E/I ratio is not just from the Glx/GABA+ ratio, but additionally, based on the steeper EEG aperiodic slope (1-20 Hz).  

As in the discussion section and response 1.4, we did not expect to see a lower Glx/GABA+ ratio in CC individuals. We discuss the possible reasons for the direction of the correlation with visual acuity and aperiodic offset during passive visual stimulation, and offer interpretations and (testable) hypotheses.

We interpret the direction of the  Glx/GABA+ correlation with visual acuity to imply that patients with highest (compensatory) balancing of the consequences of congenital blindness (hyperexcitation), in light of visual stimulation, are those who recover best. Note, the sighted control group was selected based on their “normal” vision. Thus, clinical visual acuity measures are not expected to sufficiently vary, nor have the resolution to show strong correlations with neurophysiological measures. By contrast, the CC group comprised patients highly varying in visual outcomes, and thus were ideal to investigate such correlations.

This holds for the correlation between Glx and the aperiodic intercept, as well. Previous work has suggested that the intercept of the aperiodic activity is associated with broadband spiking activity in neural circuits (Manning et al., 2009). Thus, an atypical increase of spiking activity during visual stimulation, as indirectly suggested by “old” non-human primate work on visual deprivation (Hyvärinen et al., 1981) might drive a correlation not observed in healthy populations.

In the revised manuscript, we will more clearly indicate in the discussion that these are possible post-hoc interpretations. We argue that given the lack of such studies in humans, it is all the more important that extant data be presented completely, even if the direction of the effects are not as expected.

(2.3) For these reasons, the reported findings do not allow us to draw firm conclusions on the relation between EEG parameters and E/I ratio or on the impact of early (vs. late) visual experience on the excitation/inhibition ratio of the human visual cortex.

Indeed, the correlations we have tested between the E/I ratio and EEG parameters were exploratory, and have been reported as such. The goal of our study was not to compare the effects of early vs. late visual experience. The goal was to study whether early visual experience is necessary for a typical E/I ratio in visual neural circuits. We provided clear evidence in favor of this hypothesis. Thus, the present results suggest the necessity of investigating the effects of late visual deprivation. In fact, such research is missing in permanent blindness as well.

Reviewer #3 (Public Review):

This manuscript examines the impact of congenital visual deprivation on the excitatory/inhibitory (E/I) ratio in the visual cortex using Magnetic Resonance Spectroscopy (MRS) and electroencephalography (EEG) in individuals whose sight was restored. Ten individuals with reversed congenital cataracts were compared to age-matched, normally sighted controls, assessing the cortical E/I balance and its interrelationship to visual acuity. The study reveals that the Glx/GABA ratio in the visual cortex and the intercept and aperiodic signal are significantly altered in those with a history of early visual deprivation, suggesting persistent neurophysiological changes despite visual restoration.

My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods. I have several major concerns in terms of methodological and statistical approaches along with the (over)interpretation of the results. These major concerns are detailed below.

(3.1) Variability in visual deprivation:

- The document states a large variability in the duration of visual deprivation (probably also the age at restoration), with significant implications for the sensitivity period's impact on visual circuit development. The variability and its potential effects on the outcomes need thorough exploration and discussion.

We work with a rare, unique patient population, which makes it difficult to systematically assess the effects of different visual histories while maintaining stringent inclusion criteria such as complete patterned visual deprivation at birth. Regardless, we considered the large variance in age at surgery and time since surgery as supportive of our interpretation: group differences were found despite the large variance in duration of visual deprivation. Moreover, the existing variance was used to explore possible associations between behavior and neural measures, as well as neurochemical and EEG measures.

In the revised manuscript, we will detail the advantages and disadvantages of our CC sample, with respect to duration of congenital visual deprivation.

(3.2) Sample size:

- The small sample size is a major concern as it may not provide sufficient power to detect subtle effects and/or overestimate significant effects, which then tend not to generalize to new data. One of the biggest drivers of the replication crisis in neuroscience.

We address the small sample size in our discussion, and make clear that small sample sizes were due to the nature of investigations in special populations. It is worth noting that our EEG results fully align  with those of a larger sample of CC individuals (Ossandón et al., 2023), providing us confidence about their validity and reproducibility. Moreover, our MRS results and correlations of those with EEG parameters were spatially specific to occipital cortex measures, as predicted.

The main problem with the correlation analyses between MRS and EEG measures is that the sample size is simply too small to conduct such an analysis. Moreover, it is unclear from the methods section that this analysis was only conducted in the patient group (which the reviewer assumed from the plots), and not explained why this was done only in the patient group. I would highly recommend removing these correlation analyses.

We marked the correlation analyses as exploratory; note that we do not base most of our discussion on the results of these analyses. As indicated by Reviewer 1, reporting them allows for deriving more precise hypothesis for future studies. It has to be noted that we investigate an extremely rare population, tested outside of major developed economies and dedicated neuroimaging research facilities. In addition to being a rare patient group, these individuals come from poor communities. Therefore, we consider it justified to report these correlations as exploratory, providing direction for future research.

(3.3) Statistical concerns:

- The statistical analyses, particularly the correlations drawn from a small sample, may not provide reliable estimates (see https://www.sciencedirect.com/science/article/pii/S0092656613000858, which clearly describes this problem).

It would undoubtedly be better to have a larger sample size. We nonetheless think it is of value to the research community to publish this dataset, since 10 multimodal data sets from a carefully diagnosed, rare population, representing a human model for the effects of early experience on brain development, are quite a lot.  Sample sizes in prior neuroimaging studies in transient blindness have most often ranged from n = 1 to n = 10. They nevertheless provided valuable direction for future research, and integration of results across multiple studies provides scientific insights.  

Identifying possible group differences was the goal of our study, with the correlations being an exploratory analysis, which we have clearly indicated in the methods, results and discussion.

- Statistical analyses for the MRS: The authors should consider some additional permutation statistics, which are more suitable for small sample sizes. The current statistical model (2x2) design ANOVA is not ideal for such small sample sizes. Moreover, it is unclear why the condition (EO & EC) was chosen as a predictor and not the brain region (visual & frontal) or neurochemicals. Finally, the authors did not provide any information on the alpha level nor any information on correction for multiple comparisons (in the methods section). Finally, even if the groups are matched w.r.t. age, the time between surgery and measurement, the duration of visual deprivation, (and sex?), these should be included as covariates as it has been shown that these are highly related to the measurements of interest (especially for the EEG measurements) and the age range of the current study is large.

In our ANOVA models, the neurochemicals were the outcome variables, and the conditions were chosen as predictors based on prior work suggesting that Glx/GABA+ might vary with eye closure (Kurcyus et al., 2018). The study was designed based on a hypothesis of group differences localized to the occipital cortex, due to visual deprivation. The frontal cortex voxel was chosen to indicate whether these differences were spatially specific. Therefore, we conducted separate ANOVAs based on this study design.

In the revised manuscript, we will add permutation analyses for our outcomes, as well as multiple regression models investigating whether the variance in visual history might have driven these results. Note that in the supplementary materials (S6, S7), we have reported the correlations between visual history metrics and MRS/EEG outcomes.

The alpha level used for the ANOVA models specified in the methods section was 0.05. The alpha level for the exploratory analyses reported in the main manuscript was 0.008, after correcting for (6) multiple comparisons using the Bonferroni correction, also specified in the methods. Note that the p-values following correction are expressed as multiplied by 6, due to most readers assuming an alpha level of 0.05 (see response regarding large p-values).

We used a control group matched for age and sex. Moreover, the controls were recruited and tested in the same institutes, using the same setup. We feel that we followed the gold standards for recruiting a healthy control group for a patient group.

- EEG statistical analyses: The same critique as for the MRS statistical analyses applies to the EEG analysis. In addition: was the 2x3 ANOVA conducted for EO and EC independently? This seems to be inconsistent with the approach in the MRS analyses, in which the authors chose EO & EC as predictors in their 2x2 ANOVA.

The 2x3 ANOVA was not conducted independently for the eyes open/eyes closed condition, the ANOVA conducted on the EEG metrics was 2x3 because it had group (CC, SC) and condition (eyes open (EO), eyes closed (EC) and visual stimulation (LU)) as predictors.

- Figure 4: The authors report a p-value of >0.999 with a correlation coefficient of -0.42 with a sample size of 10 subjects. This can't be correct (it should be around: p = 0.22). All statistical analyses should be checked.

As specified in the methods and figure legend, the reported p values in Figure 4 have been corrected using the Bonferroni correction, and therefore multiplied by the number of comparisons, leading to the seemingly large values.

Additionally, to check all statistical analyses, we put the manuscript through an independent Statistics Check (Nuijten & Polanin, 2020) (https://michelenuijten.shinyapps.io/statcheck-web/) and will upload the consistency report with the revised supplementary material.

- Figure 2c. Eyes closed condition: The highest score of the *Glx/GABA ratio seems to be ~3.6. In subplot 2a, there seem to be 3 subjects that show a Glx/GABA ratio score > 3.6. How can this be explained? There is also a discrepancy for the eyes-closed condition.

The three subjects that show the Glx/GABA+ ratio > 3.6 in subplot 2a are in the SC group, whereas the correlations plotted in figure 2c are only for the CC group, where the highest score is indeed ~3.6.

(3.4) Interpretation of aperiodic signal:

- Several recent papers demonstrated that the aperiodic signal measured in EEG or ECoG is related to various important aspects such as age, skull thickness, electrode impedance, as well as cognition. Thus, currently, very little is known about the underlying effects which influence the aperiodic intercept and slope. The entire interpretation of the aperiodic slope as a proxy for E/I is based on a computational model and simulation (as described in the Gao et al. paper).

Apart from the modeling work from Gao et al., multiple papers which have also been cited which used ECoG, EEG and MEG and showed concomitant changes in aperiodic activity with pharmacological manipulation of the E/I ratio (Colombo et al., 2019; Molina et al., 2020; Muthukumaraswamy & Liley, 2018). Further, several prior studies have interpreted changes in the aperiodic slope as reflective of changes in the E/I ratio, including studies of developmental groups (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Schaworonkow & Voytek, 2021) as well as patient groups (Molina et al., 2020; Ostlund et al., 2021).

In the revised manuscript, we will cite those studies not already included in the introduction.

- Especially the aperiodic intercept is a very sensitive measure to many influences (e.g. skull thickness, electrode impedance...). As crucial results (correlation aperiodic intercept and MRS measures) are facing this problem, this needs to be reevaluated. It is safer to make statements on the aperiodic slope than intercept. In theory, some of the potentially confounding measures are available to the authors (e.g. skull thickness can be computed from T1w images; electrode impedances are usually acquired alongside the EEG data) and could be therefore controlled.

All electrophysiological measures indeed depend on parameters such as skull thickness and electrode impedance. As in the extant literature using neurophysiological measures to compare brain function between patient and control groups, we used a control group matched in age/ sex, recruited in the same region, tested with the same devices, and analyzed with the same analysis pipeline. For example, impedance was kept below 10 kOhm for all subjects. There is no evidence available suggesting that congenital cataracts are associated with changes in skull thickness that would cause the observed pattern of group results. Moreover, we cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness.

- The authors wrote: "Higher frequencies (such as 20-40 Hz) have been predominantly associated with local circuit activity and feedforward signaling (Bastos et al., 2018; Van Kerkoerle et al., 2014); the increased 20-40 Hz slope may therefore signal increased spontaneous spiking activity in local networks. We speculate that the steeper slope of the aperiodic activity for the lower frequency range (1-20 Hz) in CC individuals reflects the concomitant increase in inhibition." The authors confuse the interpretation of periodic and aperiodic signals. This section refers to the interpretation of the periodic signal (higher frequencies). This interpretation cannot simply be translated to the aperiodic signal (slope).

Prior work has not always separated the aperiodic and periodic components, making it unclear what might have driven these effects in our data. The interpretation of the higher frequency range was intended to contrast with the interpretations of lower frequency range, in order to speculate as to why the two aperiodic fits might go in differing directions. We will clarify our interpretation in the revised manuscript. Note that Ossandon et al. reported highly similar results (group differences for CC individuals and for permanently congenitally blind humans) for the aperiodic activity between 20-40 Hz and oscillatory activity in the gamma range. We will allude to these findings in the revised manuscript.

- The authors further wrote: We used the slope of the aperiodic (1/f) component of the EEG spectrum as an estimate of E/I ratio (Gao et al., 2017; Medel et al., 2020; Muthukumaraswamy & Liley, 2018). This is a highly speculative interpretation with very little empirical evidence. These papers were conducted with ECoG data (mostly in animals) and mostly under anesthesia. Thus, these studies only allow an indirect interpretation by what the 1/f slope in EEG measurements is actually influenced.

Note that Muthukumaraswamy et al. (2018) used different types of pharmacological manipulations and analyzed periodic and aperiodic MEG activity in addition to monkey ECoG (Medel et al., 2020) (now published as (Medel et al., 2023)) compared EEG activity in addition to ECoG data after propofol administration. The interpretation of our results are in line with a number of recent studies in developing (Hill et al., 2022; Schaworonkow & Voytek, 2021) and special populations using EEG. As mentioned above, several prior studies have used the slope of the 1/f component/aperiodic activity as an indirect measure of the E/I ratio (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Molina et al., 2020; Ostlund et al., 2021; Schaworonkow & Voytek, 2021), including studies using scalp-recorded EEG. We will make more clear in the introduction of the revised manuscript that this metric is indirect.

While a full understanding of aperiodic activity needs to be provided, some convergent ideas have emerged . We think that our results contribute to this enterprise, since our study is, to the best of our knowledge, the first which assessed MRS measured neurotransmitter levels and EEG aperiodic activity.

(3.5) Problems with EEG preprocessing and analysis:

- It seems that the authors did not identify bad channels nor address the line noise issue (even a problem if a low pass filter of below-the-line noise was applied).

As pointed out in the methods and Figure 1, we only analyzed data from two channels, O1 and O2, neither of which were rejected for any participant. Channel rejection was performed for the larger dataset, published elsewhere (Ossandón et al., 2023; Pant et al., 2023).

In both published works, we did not consider frequency ranges above 40 Hz to avoid any possible contamination with line noise. Here, we focused on activity between 0 and 20 Hz, definitely excluding line noise contaminations. The low pass filter (FIR, 1-45 Hz) guaranteed that any spill-over effects of line noise would be restricted to frequencies just below the upper cutoff frequency.

Additionally, a prior version of the analysis used the cleanline.m function to remove line noise before filtering, and the group differences remained stable. We will report this analysis in the supplementary version of the revised manuscript. Further, both groups were measured in the same lab, making line noise as an account for the observed group effects highly unlikely. Finally, any of the exploratory MRS-EEG correlations would be hard to explain if the EEG parameters would be contaminated with line noise.

- What was the percentage of segments that needed to be rejected due to the 120μV criteria? This should be reported specifically for EO & EC and controls and patients.

The mean percentage of 1 second segments rejected for each resting state condition is below. Mean percentage of 6.25 long segments rejected in each group for the visual stimulation condition are also included, and will be added to the revised manuscript:

Author response table 3.

- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which ranged in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; Vanrullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .

- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This will be explicitly stated in the revised manuscript.

- "We excluded the alpha range (8-14 Hz) for this fit to avoid biasing the results due to documented differences in alpha activity between CC and SC individuals (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023)." This does not really make sense, as the FOOOF algorithm first fits the 1/f slope, for which the alpha activity is not relevant.

We did not use the FOOOF algorithm/toolbox in this manuscript. As stated in the methods, we used a 1/f fit to the 1-20 Hz spectrum in the log-log space, and subtracted this fit from the original spectrum to obtain the corrected spectrum. Given the pronounced difference in alpha power between groups (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023), we were concerned it might drive differences in the exponent values.  Our analysis pipeline had been adapted from previous publications of our group and other labs (Ossandón et al., 2023; Voytek et al., 2015; Waschke et al., 2017).

We have conducted the analysis with and without the exclusion of the alpha range, as well as using the FOOOF toolbox both in the 1-20 Hz and 20-40 Hz ranges (Ossandón et al., 2023); The findings of a steeper slope in the 1-20 Hz range as well as lower alpha power in CC vs SC individuals remained stable. In Ossandón et al., the comparison between the piecewise fits and FOOOF fits led the authors to use the former as it outperformed the FOOOF algorithm for their data.

- The model fits of the 1/f fitting for EO, EC, and both participant groups should be reported.

In Figure 3 of the manuscript, we depicted the mean spectra and 1/f fits for each group. We will add the fit quality metrics and show individual subjects’ fits in the revised manuscript.

(3.6) Validity of GABA measurements and results:

- According the a newer study by the authors of the Gannet toolbox (https://analyticalsciencejournals.onlinelibrary.wiley.com/doi/abs/10.1002/nbm.5076), the reliability and reproducibility of the gamma-aminobutyric acid (GABA) measurement can vary significantly depending on acquisition and modeling parameter. Thus, did the author address these challenges?

We took care of data quality while acquiring MRS data by ensuring appropriate voxel placement and linewidth prior to scanning. Acquisition as well as modeling parameters were constant for both groups, so they cannot have driven group differences.

The linked article compares the reproducibility of GABA measurement using Osprey, which was released in 2020 and uses linear combination modeling to fit the peak as opposed to Gannet’s simple peak fitting (Hupfeld et al., 2024). The study finds better test-retest reliability for Osprey compared to Gannet’s method.

As the present work was conceptualized in 2018, we used Gannet 3.0, which was the state-of-the-art edited spectral analysis toolbox at the time, and still is widely used. In the revised manuscript, we will include a supplementary section reanalyzing the main findings with Osprey.

- Furthermore, the authors wrote: "We confirmed the within-subject stability of metabolite quantification by testing a subset of the sighted controls (n=6) 2-4 weeks apart. Looking at the supplementary Figure 5 (which would be rather plotted as ICC or Blant-Altman plots), the within-subject stability compared to between-subject variability seems not to be great. Furthermore, I don't think such a small sample size qualifies for a rigorous assessment of stability.

Indeed, we did not intend to provide a rigorous assessment of within-subject stability. Rather, we aimed to confirm that data quality/concentration ratios did not systematically differ between the same subjects tested longitudinally; driven, for example, by scanner heating or time of day. As with the phantom testing, we attempted to give readers an idea of the quality of the data, as they were collected from a primarily clinical rather than a research site.

In the revised manuscript we will remove the statement regarding stability, and add the Blant-Altman plot.

- "Why might an enhanced inhibitory drive, as indicated by the lower Glx/GABA ratio" Is this interpretation really warranted, as the results of the group differences in the Glx/GABA ratio seem to be rather driven by a decreased Glx concentration in CC rather than an increased GABA (see Figure 2).

We used the Glx/GABA+ ratio as a measure, rather than individual Glx or GABA+ concentration, which did not significantly differ between groups. As detailed in Response 2.2, we think this metric aligns better with an underlying E/I balance hypothesis and has been used in many previous studies (Gao et al., 2024; Liu et al., 2015; Narayan et al., 2022; Perica et al., 2022).

Our interpretation of an enhanced inhibitory drive additionally comes from the combination of aperiodic EEG (1-20 Hz) and MRS measures, which, when considered together, are consistent with a decreased E/I ratio.

In the revised manuscript, we will rephrase this sentence accordingly. 

- Glx concentration predicted the aperiodic intercept in CC individuals' visual cortices during ambient and flickering visual stimulation. Why specifically investigate the Glx concentration, when the paper is about E/I ratio?

As stated in the methods, we exploratorily assessed the relationship between all MRS parameters (Glx, GABA+ and Glx/GABA+ ratio) with the aperiodic parameters (slope, offset), and corrected for multiple comparisons accordingly. We think this is a worthwhile analysis considering the rarity of the dataset/population (see 1.2, 1.6, 2.1 and reviewer 1’s comments about future hypotheses). We only report the Glx – aperiodic intercept correlation in the main manuscript as it survived correction for multiple comparisons.

(3.7) Interpretation of the correlation between MRS measurements and EEG aperiodic signal:

- The authors wrote: "The intercept of the aperiodic activity was highly correlated with the Glx concentration during rest with eyes open and during flickering stimulation (also see Supplementary Material S11). Based on the assumption that the aperiodic intercept reflects broadband firing (Manning et al., 2009; Winawer et al., 2013), this suggests that the Glx concentration might be related to broadband firing in CC individuals during active and passive visual stimulation." These results should not be interpreted (or with very caution) for several reasons (see also problem with influences on aperiodic intercept and small sample size). This is a result of the exploratory analyses of correlating every EEG parameter with every MRS parameter. This requires well-powered replication before any interpretation can be provided. Furthermore and importantly: why should this be specifically only in CC patients, but not in the SC control group?

We indicate clearly in all parts of the manuscript that these correlations are presented as exploratory. Further, we interpret the Glx-aperiodic offset correlation, and none of the others, as it survived the Bonferroni correction for multiple comparisons. We offer a hypothesis in the discussion section as to why such a correlation might exist in the CC but not the SC group (see response 2.2), and do not speculate further.

(3.8) Language and presentation:

- The manuscript requires language improvements and correction of numerous typos. Over-simplifications and unclear statements are present, which could mislead or confuse readers (see also interpretation of aperiodic signal).

In the revision, we will check that speculations are clearly marked and typos are removed.

- The authors state that "Together, the present results provide strong evidence for experience-dependent development of the E/I ratio in the human visual cortex, with consequences for behavior." The results of the study do not provide any strong evidence, because of the small sample size and exploratory analyses approach and not accounting for possible confounding factors.

We disagree with this statement and allude to convergent evidence of both MRS and neurophysiological measures. The latter link to corresponding results observed in a larger sample of CC individuals (Ossandón et al., 2023).

- "Our results imply a change in neurotransmitter concentrations as a consequence of *restoring* vision following congenital blindness." This is a speculative statement to infer a causal relationship on cross-sectional data.

As mentioned under 2.1, we conducted a cross-sectional study which might justify future longitudinal work. In order to advance science, new testable hypotheses were put forward at the end of a manuscript.

In the revised manuscript we will add “might imply” to better indicate the hypothetical character of this idea.

- In the limitation section, the authors wrote: "The sample size of the present study is relatively high for the rare population , but undoubtedly, overall, rather small." This sentence should be rewritten, as the study is plein underpowered. The further justification "We nevertheless think that our results are valid. Our findings neurochemically (Glx and GABA+ concentration), and anatomically (visual cortex) specific. The MRS parameters varied with parameters of the aperiodic EEG activity and visual acuity. The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) (Ossandón et al., 2023), and effects of chronological age were as expected from the literature." These statements do not provide any validation or justification of small samples. Furthermore, the current data set is a subset of an earlier published paper by the same authors "The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided.

Our intention was not to justify having a small sample, but to justify why we think the results might be valid as they align with/replicate existing literature.

In the revised manuscript, we will add a figure showing that the EEG results of the 10 subjects considered here correspond to those of the 28 other subjects of Ossandon et al. We will adapt the text accordingly, clearly stating that the pattern of EEG results of the ten subjects reported here replicate those of the 28 additional subjects of Ossandon et al. (2023).

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Author response:

Reviewer #1 (Public review):

(1) Legionella effectors are often activated by binding to eukaryote-specific host factors, including actin. The authors should test the following: a) whether Lfat1 can fatty acylate small G-proteins in vitro; b) whether this activity is dependent on actin binding; and c) whether expression of the Y240A mutant in mammalian cells affects the fatty acylation of Rac3 (Figure 6B), or other small G-proteins.

We were not able to express and purify the full-length recombinant Lfat1 to perform fatty acylation of small GTPases in vitro. However, in cellulo overexpression of the Y240A mutant still retained ability to fatty acylate Rac3 and another small GTPase RheB (see Author response image 1 below). We postulate that under infection conditions, actin-binding might be required to fatty acylate certain GTPases due to the small amount of effector proteins that secreted into the host cell.

Author response image 1.

(2) It should be demonstrated that lysine residues on small G-proteins are indeed targeted by Lfat1. Ideally, the functional consequences of these modifications should also be investigated. For example, does fatty acylation of G-proteins affect GTPase activity or binding to downstream effectors?

We have mutated K178 on RheB and showed that this mutation abolished its fatty acylation by Lfat1 (see Author response image 2 below). We were not able to test if fatty acylation by Lfat1 affect downstream effector binding.

Author response image 2.

(3) Line 138: Can the authors clarify whether the Lfat1 ABD induces bundling of F-actin filaments or promotes actin oligomerization? Does the Lfat1 ABD form multimers that bring multiple filaments together? If Lfat1 induces actin oligomerization, this effect should be experimentally tested and reported. Additionally, the impact of Lfat1 binding on actin filament stability should be assessed. This is particularly important given the proposed use of the ABD as an actin probe.

The ABD domain does not form oligomer as evidenced by gel filtration profile of the ABD domain. However, we do see F-actin bundling in our in vitro -F-actin polymerization experiment when both actin and ABD are in high concentration (data not shown). Under low concentration of ABD, there is not aggregation/bundling effect of F-actin.

(4) Line 180: I think it's too premature to refer to the interaction as having "high specificity and affinity." We really don't know what else it's binding to.

We have revised the text and reworded the sentence by removing "high specificity and affinity."

(5) The authors should reconsider the color scheme used in the structural figures, particularly in Figures 2D and S4.

Not sure the comments on the color scheme of the structure figures.

(6) In Figure 3E, the WT curve fits the data poorly, possibly because the actin concentration exceeds the Kd of the interaction. It might fit better to a quadratic.

We have performed quadratic fitting and replaced Figure 3E.

(7) The authors propose that the individual helices of the Lfat1 ABD could be expressed on separate proteins and used to target multi-component biological complexes to F-actin by genetically fusing each component to a split alpha-helix. This is an intriguing idea, but it should be tested as a proof of concept to support its feasibility and potential utility.

It is a good suggestion. We plan to thoroughly test the feasibility of this idea as one of our future directions.

(7) The plot in Figure S2D appears cropped on the X-axis or was generated from a ~2× binned map rather than the deposited one (pixel size ~0.83 Å, plot suggests ~1.6 Å). The reported pixel size is inconsistent between the Methods and Table 1-please clarify whether 0.83 Å refers to super-resolution.

Yes, 0.83 Å is super-resolution. We have updated in the cryoEM table

Reviewer #2 (Public review):

Weaknesses:

(1) The authors should use biochemical reactions to analyze the KFAT of Llfat1 on one or two small GTPases shown to be modified by this effector in cellulo. Such reactions may allow them to determine the role of actin binding in its biochemical activity. This notion is particularly relevant in light of recent studies that actin is a co-factor for the activity of LnaB and Ceg14 (PMID: 39009586; PMID: 38776962; PMID: 40394005). In addition, the study should be discussed in the context of these recent findings on the role of actin in the activity of L. pneumophila effectors.

We have new data showed that Actin binding does not affect Lfat1 enzymatic activity. (see figure; response to Reviewer #1). We have added this new data as Figure S7 to the paper. Accordingly, we also revised the discussion by adding the following paragraph.

“The discovery of Lfat1 as an F-actin–binding lysine fatty acyl transferase raised the intriguing question of whether its enzymatic activity depends on F-actin binding. Recent studies have shown that other Legionella effectors, such as LnaB and Ceg14, use actin as a co-factor to regulate their activities. For instance, LnaB binds monomeric G-actin to enhance its phosphoryl-AMPylase activity toward phosphorylated residues, resulting in unique ADPylation modifications in host proteins (Fu et al, 2024; Wang et al, 2024). Similarly, Ceg14 is activated by host actin to convert ATP and dATP into adenosine and deoxyadenosine monophosphate, thereby modulating ATP levels in L. pneumophila–infected cells (He et al, 2025). However, this does not appear to be the case for Lfat1. We found that Lfat1 mutants defective in F-actin binding retained the ability to modify host small GTPases when expressed in cells (Figure S7). These findings suggest that, rather than serving as a co-factor, F-actin may serve to localize Lfat1 via its actin-binding domain (ABD), thereby confining its activity to regions enriched in F-actin and enabling spatial specificity in the modification of host targets.”

(2) The development of the ABD domain of Llfat1 as an F-actin domain is a nice extension of the biochemical and structural experiments. The authors need to compare the new probe to those currently commonly used ones, such as Lifeact, in labeling of the actin cytoskeleton structure.

We fully agree with the reviewer’s insightful suggestion. However, a direct comparison of the Lfat1 ABD domain with commonly used actin probes such as Lifeact, as well as evaluation of the split α-helix probe (as suggested by Reviewer #1), would require extensive and technically demanding experiments. These are important directions that we plan to pursue in future studies.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study reveals that TRPV1 signaling plays a key role in tympanic membrane (TM) healing by promoting macrophage recruitment and angiogenesis. Using a mouse TM perforation model, researchers found that blood-derived macrophages accumulated near the wound, driving angiogenesis and repair. TRPV1-expressing nerve fibers triggered neuroinflammatory responses, facilitating macrophage recruitment. Genetic Trpv1 mutation reduced macrophage infiltration, angiogenesis, and delayed healing. These findings suggest that targeting TRPV1 or stimulating sensory nerve fibers could enhance TM repair, improve blood flow, and prevent infections. This offers new therapeutic strategies for TM perforations and otitis media in clinical settings. This is an excellent and high-quality study that provides valuable insights into the mechanisms underlying TM wound healing.

Strengths:

The work is particularly important for elucidating the cellular and molecular processes involved in TM repair. However, there are several concerns about the current version.

We sincerely thank Reviewer #1 for their time and effort in evaluating and improving our study. Below, we are pleased to address the Reviewer's concerns point by point.

Weaknesses:

Major concerns

(1) The method of administration will be a critical factor when considering potential therapeutic strategies to promote TM healing. It would be beneficial if the authors could discuss possible delivery methods, such as topical application, transtympanic injection, or systemic administration, and their respective advantages and limitations for targeting TRPV1 signaling. For example, Dr. Kanemaru and his colleagues have proposed the use of Trafermin and Spongel to regenerate the eardrum.

We are grateful to the reviewer for raising this important point. While the present study primarily focuses on the mechanistic role of TRPV1 in TM repair, we agree that the mode of therapeutic delivery will be pivotal in translating these findings into clinical practice. In response, we will expand the discussion to explore possible delivery methods—such as topical application, transtympanic injection, and systemic routes—along with their respective benefits and challenges. We will also cite the work by Dr. Kanemaru and colleagues as an example of how local delivery systems may facilitate TM regeneration.

(2) The authors appear to have used surface imaging techniques to observe the TM. However, the TM consists of three distinct layers: the epithelial layer, the fibrous middle layer, and the inner mucosal layer. The authors should clarify whether the proposed mechanism involving TRPV1-mediated macrophage recruitment and angiogenesis is limited to the epithelial layer or if it extends to the deeper layers of the TM.

We apologize for any confusion caused by our previous description. In our study, we utilized Z-stack confocal imaging to capture the full thickness of the TM, as illustrated in Author response image 1 (reconstructed from the acquired Z-sections). This imaging technique allowed us to encompass all three layers of the TM entirely. Each sample was imaged using a 10X objective on an Olympus fluorescence microscope. Given the conical shape and size of the TM, we imaged it in four quadrants, acquiring approximately 30 optical sections (with a 3 µm step) per region. Each acquired images were projected and exported using FV10ASW 4.2 Viewer, then stitched together using Photoshop. The resulting Z-stack projections enabled us to visualize the distribution of macrophages, angiogenesis, and the localization of nerve fibers throughout the TM. We will include this detailed methodology in our revision to clarify any potential confusion.

Author response image 1.

Representative confocal images showing one quadrant of the TM collected from collected from CSR1F^EGFP bone marrow transplanted mouse at day 7 post-perforation. (A-B) 3D-rendered views from different angles reveal the close spatial relationship between CSF1R^EGFP cells (green) and blood vessels (red) within the TM. (C) Cross-sectional view highlights the depth-wise distribution of CSF1R^EGFP cells (green) and blood vessels (red) across the layered TM architecture. All images were processed using Imaris Viewer x64 (version 10.2.0).

Minor concerns

In Figure 8, the schematic illustration presents a coronal section of the TM. However, based on the data provided in the manuscript, it is unclear whether the authors directly obtained coronal images in their study. To enhance the clarity and impact of the schematic, it would be helpful to include representative images of coronal sections showing macrophage infiltration, angiogenesis, and nerve fiber distribution in the TM.

As noted above, we utilized Z-stack confocal imaging to capture the full thickness of the TM, enabling us to visualize structures across all three layers. This approach ensured that all layers were included in our analysis. Due to the thin and curved nature of the TM, traditional cross-sectional imaging often struggles to clearly depict the spatial relationships between macrophages, blood vessels, and nerve fibers, especially at low magnification as shown in Author response image 2. In response to the reviewer's suggestion, we will include representative coronal images in the revised manuscript to better illustrate the distribution of these structures at higher magnification.

Author response image 2.

Confocal images of eardrum cross-sections collected at day 1 (A), 3 (B), and 7 (C) post perforation to demonstrate the wound healing processes.

Reviewer #2 (Public review):

Summary:

This study examines the role of TRPV1 signaling in the recruitment of monocyte-derived macrophages and the promotion of angiogenesis during tympanic membrane (TM) wound healing. The authors use a combination of genetic mouse models, macrophage depletion, and transcriptomic approaches to suggest that neuronal TRPV1 activity contributes to macrophage-driven vascular responses necessary for tissue repair.

Strengths:

(1) The topic of neuroimmune interactions in tissue regeneration is of interest and underexplored in the context of the TM, which presents a unique model due to its anatomical features.

(2) The use of reporter mice and bone marrow chimeras allows for some dissection of immune cell origin.

(3) The authors incorporate transcriptomic data to contextualize inflammatory and angiogenic processes during wound healing.

We sincerely thank Reviewer #2 for their time and effort in improving our study and recognizing its strengths. Below, we are pleased to address the reviewer's concerns point by point.

Weaknesses:

(1) The primary claims of the manuscript are not convincingly supported by the evidence presented. Most of the data are correlative in nature, and no direct mechanistic experiments are included to establish causality between TRPV1 signaling and macrophage recruitment or function.

We appreciate Reviewer #2's perspective on the lack of molecular mechanisms linking TRPV1 signaling and macrophages. However, our data demonstrates that TRPV1 mutations significantly affect macrophage recruitment and angiogenesis. This initial study primarily focuses on the intriguing phenomenon of how sensory nerve fibers are involved in eardrum immunity and wound healing, an area that has not been clearly reported in the literature before. We believe that further research is necessary to explore this topic in greater depth.

(2) Functional validation of key molecular players (such as Tac1 or Spp1) is lacking, and their roles are inferred primarily from gene expression data rather than experimentally tested.

Although we have identified the TAC1 and SPP1 signals as potentially important for TM wound healing for the first time, we agree with the Reviewer's view regarding the lack of molecular mechanisms explored in this study. We have not yet tested the downstream signaling pathways, but we plan to investigate them in a series of future studies. As this is an early report, we will continue to explore these signals and their potential clinical applications based on our initial findings moving forward.

(3) The reuse of publicly available scRNA-seq data is not sufficiently integrated or extended to yield new biological insights, and it remains largely descriptive.

We appreciate Reviewer #2 for highlighting this point. Leveraging publicly available scRNA-seq databases and established analysis pipelines not only saves time and resources—my lab recently collected macrophages from the eardrums of postnatal P15 mice, with each trial requiring 20 eardrums from 10 animals to obtain a sufficient number of cells—but also allows researchers to build on previous work and focus on new biological questions without the need to repeat experiments. A prior study conducted by Dr. Tward and his team utilized scRNA-seq data to make initial discoveries related to eardrum wound healing, primarily focusing on epithelial cells rather than macrophages. We are building on their raw data to uncover new biological insights regarding macrophages, even though we have not yet tested the unidentified signals, which we believe will be valuable to our peers.

(4) The macrophage depletion model (CX3CR1CreER; iDTR) lacks specificity, and possible off-target or systemic effects are not addressed.

We agree with reviewer #2, although macrophage depletion model used in our study is a standard and well-used animal model (Shi, Hua et al. 2018), which has been used by many other laboratories, it is important to note that any macrophage depletion model may have potential issues. We will discuss this in our revision.

(5) Several interpretations of the data appear overstated, particularly regarding the necessity of TRPV1 for monocyte recruitment and wound healing.

We thank the reviewer for pointing this out. We will revise our manuscript where it is overstated accordingly.

(6) Overall, the study appears to apply known concepts - namely, TRPV1-mediated neurogenic inflammation and macrophage-driven angiogenesis - to a new anatomical site without providing new mechanistic insight or advancing the field substantially.

Although our study may not seem highly innovative at first glance, it reveals a previously unknown role of the TRPV1 pain signaling pathway in promoting eardrum healing for the first time. This healing process includes the recruitment of monocyte-derived macrophages and the formation of new blood vessels (angiogenesis). While this process has been documented in other organs, most research on macrophage-driven angiogenesis has been conducted using in vitro models, with very few studies demonstrating this process in vivo. Our findings could lead to new translational opportunities, especially considering that tympanic membrane perforation, along with damage-induced otitis media and conductive hearing loss, are common clinical issues affecting millions of people worldwide. Targeting TRPV1 signaling could enhance tympanic membrane immunity, improve blood circulation, promote the repair of damaged tympanic membranes, and ultimately prevent middle ear infections—an idea that has not been previously proposed.

Overall:

While the study addresses an interesting topic, the current version does not provide sufficiently strong or novel evidence to support its major conclusions. Additional mechanistic experiments and more rigorous validation would be necessary to substantiate the proposed model and clarify the relevance of the findings beyond this specific tissue context.

We greatly thank the two reviewers for their helpful critiques to improve our study. We especially thank the Section Editors for their insightful and constructive comments on this initial study.

References:

Shi, J., L. Hua, D. Harmer, P. Li and G. Ren (2018). "Cre Driver Mice Targeting Macrophages." Methods Mol Biol 1784: 263-275.

Author response:

Reviewer #1 (Public review):

Summary:

This article investigates the origin of movement slowdown in weightlessness by testing two possible hypotheses: the first is based on a strategic and conservative slowdown, presented as a scaling of the motion kinematics without altering its profile, while the second is based on the hypothesis of a misestimation of effective mass by the brain due to an alteration of gravity-dependent sensory inputs, which alters the kinematics following a controller parameterization error.

Strengths:

The article convincingly demonstrates that trajectories are affected in 0g conditions, as in previous work. It is interesting, and the results appear robust. However, I have two major reservations about the current version of the manuscript that prevent me from endorsing the conclusion in its current form.

Weaknesses:

(1) First, the hypothesis of a strategic and conservative slow down implicitly assumes a similar cost function, which cannot be guaranteed, tested, or verified. For example, previous work has suggested that changing the ratio between the state and control weight matrices produced an alteration in movement kinematics similar to that presented here, without changing the estimated mass parameter (Crevecoeur et al., 2010, J Neurophysiol, 104 (3), 1301-1313). Thus, the hypothesis of conservative slowing cannot be rejected. Such a strategy could vary with effective mass (thus showing a statistical effect), but the possibility that the data reflect a combination of both mechanisms (strategic slowing and mass misestimation) remains open.

We test whether changing the ratio between the state and control weight matrices can generate the observed effect. As shown in Author response image 1 and Author response image 2, the cost function change cannot produce a reduced peak velocity/acceleration and their timing advance simultaneously, but a mass estimation change can. In other words, using mass underestimation alone can explain the two key findings, amplitude reduction and timing advance. Yes, we cannot exclude the possibility of a change in cost function on top of the mass underestimation, but the principle of Occam’s Razor would support to adhering to a simple explanation, i.e., using body mass underestimation to explain the key findings. We will include our exploration on possible changes in cost function in the revision (in the Supplemental Materials).

Author response image 1.

Simulation using an altered cost function with α = 3.0. Panels A, B, and E show simulated position, velocity, and acceleration profiles, respectively, for the three movement directions. Solid lines correspond to pre- and post-exposure conditions, while dashed lines represent the in-flight condition. Panels C and D display the peak velocity and its timing across the three phases (Pre, In, Post), and Panels F and G show the corresponding peak acceleration and its timing. Note, varying the cost function, while leading to reduced peak velocity/acceleration, leads to an erroneous prediction of delayed timing of peak velocity/acceleration.

Author response image 2.

Simulation results using a cost function with α = 0.3. The format is the same as in Author response image 1. Note, this ten-fold decrease in α, while finally getting the timing of peak velocity/acceleration right (advanced or reduced), leads to an erroneous prediction of increased peak velocity/acceleration.

(2) The main strength of the article is the presence of directional effects expected under the hypothesis of mass estimation error. However, the article lacks a clear demonstration of such an effect: indeed, although there appears to be a significant effect of direction, I was not sure that this effect matched the model's predictions. A directional effect is not sufficient because the model makes clear quantitative predictions about how this effect should vary across directions. In the absence of a quantitative match between the model and the data, the authors' claims regarding the role of misestimating the effective mass remain unsupported.

Our paper does not aim to quantitatively reproduce human reaching movements in microgravity. We will make this more clearly in the revision.

(1) The model is a simplification of the actual situation. For example, the model simulates an ideal case of moving a point mass (effective mass) without friction and without considering Coriolis and centripetal torques, while the actual situation is that people move their finger across a touch screen. The two-link arm model assumes planar movements, but our participants move their hand on a table top without vertical support to constrain their movement in 2D.

(2) Our study merely uses well-established (though simplified) models to qualitatively predict the overall behavioral patterns if mass underestimation is at play. For this purpose, the results are well in line with models’ qualitative predictions: we indeed confirm that key kinematic features (peak velocity and acceleration) follow the same ranking order of movement direction conditions as predicted.

(3) Using model simulation to qualitatively predict human behavioral patterns is a common practice in motor control studies, prominent examples including the papers on optimal feedback control (Todorov, 2004 and 2005) and movement vigor (Shadmehr et al., 2016). In fact, our model was inspired by the model in the latter paper.

Citations:

Todorov, E. (2004). Optimality principles in sensorimotor control. Nature Neuroscience, 7(9), 907.

Todorov, E. (2005). Stochastic optimal control and estimation methods adapted to the noise characteristics of the sensorimotor system. Neural Computation, 17(5), 1084–1108.

Shadmehr, R., Huang, H. J., & Ahmed, A. A. (2016). A Representation of Effort in Decision-Making and Motor Control. Current Biology: CB, 26(14), 1929–1934.

In general, both the hypotheses of slowing motion (out of caution) and misestimating mass have been put forward in the past, and the added value of this article lies in demonstrating that the effect depended on direction. However, (1) a conservative strategy with a different cost function can also explain the data, and (2) the quantitative match between the directional effect and the model's predictions has not been established.

Specific points:

(1) I noted a lack of presentation of raw kinematic traces, which would be necessary to convince me that the directional effect was related to effective mass as stated.

We are happy to include exemplary speed and acceleration trajectories. One example subject’s detailed trajectories are shown below and will be included in the revision. The reduced and advanced velocity/acceleration peaks are visible in typical trials.

Author response image 3.

Hand speed profiles (upper panels), hand acceleration profiles (middle panels) and speed profiles of the primary submovements (lower panels) towards different directions from an example participant.

(2) The presentation and justification of the model require substantial improvement; the reason for their presence in the supplementary material is unclear, as there is space to present the modelling work in detail in the main text. Regarding the model, some choices require justification: for example, why did the authors ignore the nonlinear Coriolis and centripetal terms?

Response: In brief, our simulations show that Coriolis and centripetal forces, despite having some directional anisotropy, only have small effects on predicted kinematics (see our responses to Reviewer 2). We will move descriptions of the model into the main text with more justifications for using a simple model.

(3) The increase in the proportion of trials with subcomponents is interesting, but the explanatory power of this observation is limited, as the initial percentage was already quite high (from 60-70% during the initial study to 70-85% in flight). This suggests that the potential effect of effective mass only explains a small increase in a trend already present in the initial study. A more critical assessment of this result is warranted.

Response: Indeed, the percentage of submovements only increases slightly, but the more important change is that the IPI (the inter-peak interval between submovements) also increases at the same time. Moreover, it is the effect of IPI that significantly predicts the duration increase in our linear mixed model. We will highlight this fact in our revision to avoid confusion.

Reviewer #2 (Public review):

This study explores the underlying causes of the generalized movement slowness observed in astronauts in weightlessness compared to their performance on Earth. The authors argue that this movement slowness stems from an underestimation of mass rather than a deliberate reduction in speed for enhanced stability and safety.

Overall, this is a fascinating and well-written work. The kinematic analysis is thorough and comprehensive. The design of the study is solid, the collected dataset is rare, and the model tends to add confidence to the proposed conclusions. That being said, I have several comments that could be addressed to consolidate interpretations and improve clarity.

Main comments:

(1) Mass underestimation

a) While this interpretation is supported by data and analyses, it is not clear whether this gives a complete picture of the underlying phenomena. The two hypotheses (i.e., mass underestimation vs deliberate speed reduction) can only be distinguished in terms of velocity/acceleration patterns, which should display specific changes during the flight with a mass underestimation. The experimental data generally shows the expected changes but for the 45{degree sign} condition, no changes are observed during flight compared to the pre- and post-phases (Figure 4). In Figure 5E, only a change in the primary submovement peak velocity is observed for 45{degree sign}, but this finding relies on a more involved decomposition procedure. It suggests that there is something specific about 45{degree sign} (beyond its low effective mass). In such planar movements, 45{degree sign} often corresponds to a movement which is close to single-joint, whereas 90{degree sign} and 135{degree sign} involve multi-joint movements. If so, the increased proportion of submovements in 90{degree sign} and 135{degree sign} could indicate that participants had more difficulties in coordinating multi-joint movements during flight. Besides inertia, Coriolis and centripetal effects may be non-negligible in such fast planar reaching (Hollerbach & Flash, Biol Cyber, 1982) and, interestingly, they would also be affected by a mass underestimation (thus, this is not necessarily incompatible with the author's view; yet predicting the effects of a mass underestimation on Coriolis/centripetal torques would require a two-link arm model). Overall, I found the discrepancy between the 45{degree sign} direction and the other directions under-exploited in the current version of the article. In sum, could the corrective submovements be due to a misestimation of Coriolis/centripetal torques in the multi-joint dynamics (caused specifically -or not- by a mass underestimation)?

We agree that the effect of mass underestimation is less in the 45° direction than the other two directions, possibly related to its reliance on single-joint (elbow) as opposed to two-joints (elbow and shoulder) movements. Plus, movement correction using one joint is probably easier (as also suggested by another reviewer), this possibility will be further discussed in the revision. However, we find that our model simplification (excluding Coriolis and centripetal torques) does not affect our main conclusions at all. First, we performed a simple simulation and found that, under the current optimal hand trajectory, incorporating Coriolis and centripetal torques has only a limited impact on the resulting joint torques (see simulations in Author response image 4). One reason is that we used smaller movements than Hallerbach & Flash did. In addition, we applied an optimal feedback control model to a more realistic 2-joint arm configuration. Despite its simplicity, this model produced a speed profile consistent with our current predictions and made similar predictions regarding the effects of mass underestimation (Author response image 5). We will provide a more realistic 2-joint arm model muscle dynamics in the revision to improve the simulation further, but the message will be same: including or excluding Coriolis and centripetal torques will not affect the theoretical predictions about mass underestimation. Second, as the reviewer correctly pointed out, the mass (and its underestimation) also affects these two torque terms, thus its effect on kinematic measures is not affected much even with the full model.

Author response image 4.

Joint angles and joint torque of shoulder and elbow with simulated trajectories towards different directions. A. Shoulder (green) and elbow (blue) angles change with time for the 45° movement direction. B. Components of joint interaction torques at the shoulder. Solid line: net torque at the shoulder; dotted line: shoulder inertia torque; dashed line: shoulder Coriolis and centripetal torque. C. Same plot as B for the elbow joint. D–F. Coriolis and centripetal components in the full 360° workspace, beyond three movement directions (45°, 90°, and 135°). D. Net torque. E. Inertial torque. F. Combined Coriolis and centripetal torque. Note the polar plots of Coriolis/centripetal torques (F) have a scale that is two magnitudes smaller than that of inertial torque in our simulation. All torques were simulated with the optimal movement duration. Torques were squared and integrated over each trajectory.

Author response image 5.

Comparison between simulation results from the full model with the addition of Coriolis/centripetal torques (left) and the simplified model (right). The position profiles (top) and the corresponding speed profiles low) are shown. Solid lines are for normal mass estimation and dashed lines for mass underestimation in microgravity. The three colors represent three movement directions (dark red: 45°, red: 90°, yellow: 135°). The full model used a 2-link arm model without realistic muscle dynamics yet (will include in the formal revision) thus the speed profile is not smooth. Importantly, the full model also predict the same effect of mass underestimation, i.e., reduced peak velocity/acceleration and their timing advance.

b) Additionally, since the taikonauts are tested after 2 or 3 weeks in flight, one could also assume that neuromuscular deconditioning explains (at least in part) the general decrease in movement speed. Can the authors explain how to rule out this alternative interpretation? For instance, weaker muscles could account for slower movements within a classical time-effort trade-off (as more neural effort would be needed to generate a similar amount of muscle force, thereby suggesting a purposive slowing down of movement). Therefore, could the observed results (slowing down + more submovements) be explained by some neuromuscular deconditioning combined with a difficulty in coordinating multi-joint movements in weightlessness (due to a misestimation or Coriolis/centripetal torques) provide an alternative explanation for the results?

Response: Neuromuscular deconditioning is indeed a space or microgravity effect; thanks for bringing this up as we omitted the discussion of its possible contribution in the initial submission. However, muscle weakness is less for upper-limb muscles than for postural and lower-limb muscles (Tesch et al., 2005). The handgrip strength decreases 5% to 15% after several months (Moosavi et al., 2021); shoulder and elbow muscles atrophy, though not directly measured, was estimated to be minimal (Shen et al., 2017). The muscle weakness is unlikely to play a major role here since our reaching task involves small movements (~12cm) with joint torques of a magnitude of ~2N·m. Coriolis/centripetal torques does not affect the putative mass effect (as shown above simulations). The reviewer suggests that their poor coordination in microgravity might contribute to slowing down + more submovements. Poor coordination is an umbrella term for any motor control problems, and it can explain any microgravity effect. The feedforward control changes caused by mass underestimation can also be viewed as poor coordination. If we limit it as the coordination of the two joints or coordinating Coriolis/centripetal torques, we should expect to see some trajectory curvature changes in microgravity. However, we further analyzed our reaching trajectories and found no sign of curvature increase in our large collection of reaching movements. We probably have the largest dataset of reaching movements collected in microgravity thus far, given that we had 12 taikonauts and each of them performed about 480 to 840 reaching trials during their spaceflight. We believe the probability of Type II error is quite low here. We will include descriptive statistics of these new analyses in our revision.

Citation: Tesch, P. A., Berg, H. E., Bring, D., Evans, H. J., & LeBlanc, A. D. (2005). Effects of 17-day spaceflight on knee extensor muscle function and size. European journal of applied physiology, 93(4), 463-468.

Moosavi, D., Wolovsky, D., Depompeis, A., Uher, D., Lennington, D., Bodden, R., & Garber, C. E. (2021). The effects of spaceflight microgravity on the musculoskeletal system of humans and animals, with an emphasis on exercise as a countermeasure: A systematic scoping review. Physiological Research, 70(2), 119.

Shen, H., Lim, C., Schwartz, A. G., Andreev-Andrievskiy, A., Deymier, A. C., & Thomopoulos, S. (2017). Effects of spaceflight on the muscles of the murine shoulder. The FASEB Journal, 31(12), 5466.

(2) Modelling

a) The model description should be improved as it is currently a mix of discrete time and continuous time formulations. Moreover, an infinite-horizon cost function is used, but I thought the authors used a finite-horizon formulation with the prefixed duration provided by the movement utility maximization framework of Shadmehr et al. (Curr Biol, 2016). Furthermore, was the mass underestimation reflected both in the utility model and the optimal control model? If so, did the authors really compute the feedback control gain with the underestimated mass but simulate the system with the real mass? This is important because the mass appears both in the utility framework and in the LQ framework. Given the current interpretations, the feedforward command is assumed to be erroneous, and the feedback command would allow for motor corrections. Therefore, it could be clarified whether the feedback command also misestimates the mass or not, which may affect its efficiency. For instance, if both feedforward and feedback motor commands are based on wrong internal models (e.g., due to the mass underestimation), one may wonder how the astronauts would execute accurate goal-directed movements.

b) The model seems to be deterministic in its current form (no motor and sensory noise). Since the framework developed by Todorov (2005) is used, sensorimotor noise could have been readily considered. One could also assume that motor and sensory noise increase in microgravity, and the model could inform on how microgravity affects the number of submovements or endpoint variance due to sensorimotor noise changes, for instance.

c) Finally, how does the model distinguish the feedforward and feedback components of the motor command that are discussed in the paper, given that the model only yields a feedback control law? Does 'feedforward' refer to the motor plan here (i.e., the prefixed duration and arguably the precomputed feedback gain)?

We appreciate these very helpful suggestions about our model presentation. Indeed, our initial submission did not give detailed model descriptions in the main text, due to text limits for early submissions. We actually used a finite-horizon framework throughout, with a pre-specified duration derived from the utility model. In the revision, we will make that point clear, and we will also revise the Methods section to explicitly distinguish feedforward vs. feedback components, clarify the use of mass underestimation in both utility and control models, and update the equations accordingly.

(3) Brevity of movements and speed-accuracy trade-off

The tested movements are much faster (average duration approx. 350 ms) than similar self-paced movements that have been studied in other works (e.g., Wang et al., J Neurophysiology, 2016; Berret et al., PLOS Comp Biol, 2021, where movements can last about 900-1000 ms). This is consistent with the instructions to reach quickly and accurately, in line with a speed-accuracy trade-off. Was this instruction given to highlight the inertial effects related to the arm's anisotropy? One may however, wonder if the same results would hold for slower self-paced movements (are they also with reduced speed compared to Earth performance?). Moreover, a few other important questions might need to be addressed for completeness: how to ensure that astronauts did remember this instruction during the flight? (could the control group move faster because they better remembered the instruction?). Did the taikonauts perform the experiment on their own during the flight, or did one taikonaut assume the role of the experimenter?

Thanks for highlighting the brevity of movements in our experiment. Our intention in emphasizing fast movements is to rigorously test whether movement is indeed slowed down in microgravity. The observed prolonged movement duration clearly shows that microgravity affects people’s movement duration, even when they are pushed to move fast. The second reason for using fast movement is to highlight that feedforward control is affected in microgravity. Mass underestimation specifically affects feedforward control in the first place. Slow movement would inevitably have online corrections that might obscure the effect of mass underestimation. Note that movement slowing is not only observed in our speed-emphasized reaching task, but also in whole-arm pointing in other astronauts studies (Berger, 1997; Sangals, 1999), which have been quoted in our paper. We thus believe these findings are generalizable.

Regarding the consistency of instructions: all our experiments conducted in the Tiangong space station were monitored in real time by experimenters in the Control Center located in Beijing. The task instructions were presented on the initial display of the data acquisition application and ample reading time was allowed. In fact, all the pre-, in-, and post-flight test sessions were administered by the same group of experimenters with the same instruction. It is common that astronauts serve both as participants and experimenters at the same time. And, they were well trained for this type of role on the ground. Note that we had multiple pre-flight test sessions to familiarize them with the task. All these rigorous measures were in place to obtain high-quality data. We will include these experimental details and the rationales for emphasizing fast movements in the revision.

Citations:

Berger, M., Mescheriakov, S., Molokanova, E., Lechner-Steinleitner, S., Seguer, N., & Kozlovskaya, I. (1997). Pointing arm movements in short- and long-term spaceflights. Aviation, Space, and Environmental Medicine, 68(9), 781–787.

Sangals, J., Heuer, H., Manzey, D., & Lorenz, B. (1999). Changed visuomotor transformations during and after prolonged microgravity. Experimental Brain Research. Experimentelle Hirnforschung. Experimentation Cerebrale, 129(3), 378–390.

(4) No learning effect

This is a surprising effect, as mentioned by the authors. Other studies conducted in microgravity have indeed revealed an optimal adaptation of motor patterns in a few dozen trials (e.g., Gaveau et al., eLife, 2016). Perhaps the difference is again related to single-joint versus multi-joint movements. This should be better discussed given the impact of this claim. Typically, why would a "sensory bias of bodily property" persist in microgravity and be a "fundamental constraint of the sensorimotor system"?

We believe the differences between our study and Gaveau et al.’s study cannot be simply attributed to single-joint versus multi-joint movements. One of the most salient differences is that their adaptation is about incorporating microgravity in control for minimizing effort, while our adaptation is about rightfully perceiving body mass. We will elaborate on possible reasons for the lack of learning in the light of this previous study.

We can elaborate on “sensory bias” and “fundamental constraint of the sensorimotor system”. If an inertial change is perceived (like an extra weight attached to the forearm, as in previous motor adaptation studies), people can adapt their reaching in tens of trials. In this case, sensory cues are veridical as they correctly inform about the inertial perturbation. However, in microgravity, reduced gravitational pull and proprioceptive inputs constantly inform the controller that the body mass is less than its actual magnitude. In other words, sensory cues in space are misleading for estimating body mass. The resulting sensory bias prevents the sensorimotor system from correctly adapt. Our statement was too brief in the initial submission; we will expand it in the revision.

Reviewer #3 (Public review):

Summary:

The authors describe an interesting study of arm movements carried out in weightlessness after a prolonged exposure to the so-called microgravity conditions of orbital spaceflight. Subjects performed radial point-to-point motions of the fingertip on a touch pad. The authors note a reduction in movement speed in weightlessness, which they hypothesize could be due to either an overall strategy of lowering movement speed to better accommodate the instability of the body in weightlessness or an underestimation of body mass. They conclude for the latter, mainly based on two effects. One, slowing in weightlessness is greater for movement directions with higher effective mass at the end effector of the arm. Two, they present evidence for an increased number of corrective submovements in weightlessness. They contend that this provides conclusive evidence to accept the hypothesis of an underestimation of body mass.

Strengths:

In my opinion, the study provides a valuable contribution, the theoretical aspects are well presented through simulations, the statistical analyses are meticulous, the applicable literature is comprehensively considered and cited, and the manuscript is well written.

Weaknesses:

Nevertheless, I am of the opinion that the interpretation of the observations leaves room for other possible explanations of the observed phenomenon, thus weakening the strength of the arguments.

First, I would like to point out an apparent (at least to me) divergence between the predictions and the observed data. Figures 1 and S1 show that the difference between predicted values for the 3 movement directions is almost linear, with predictions for 90º midway between predictions for 45º and 135º. The effective mass at 90º appears to be much closer to that of 45º than to that of 135º (Figure S1A). But the data shown in Figure 2 and Figure 3 indicate that movements at 90º and 135º are grouped together in terms of reaction time, movement duration, and peak acceleration, while both differ significantly from those values for movements at 45º.

Furthermore, in Figure 4, the change in peak acceleration time and relative time to peak acceleration between 1g and 0g appears to be greater for 90º than for 135º, which appears to me to be at least superficially in contradiction with the predictions from Figure S1. If the effective mass is the key parameter, wouldn't one expect as much difference between 90º and 135º as between 90º and 45º? It is true that peak speed (Figure 3B) and peak speed time (Figure 4B) appear to follow the ordering according to effective mass, but is there a mathematical explanation as to why the ordering is respected for velocity but not acceleration? These inconsistencies weaken the author's conclusions and should be addressed.

Indeed, the model predicts an almost equal separation between 45° and 90° and between 90° and 135°, while the data indicate that the spacing between 45° and 90° is much smaller than between 90° and 135°. We do not regard the divergence as evidence undermining our main conclusion since 1) the model is a simplification of the actual situation. For example, the model simulates an ideal case of moving a point mass (effective mass) without friction and without considering Coriolis and centripetal torques. 2) Our study does not make quantitative predictions of all the key kinematic measures; that will require model fitting and parameter estimation; instead, our study uses well-established (though simplified) models to qualitatively predict the overall behavioral pattern we would observe. For this purpose, our results are well in line with our expectations: though we did not find equal spacing between direction conditions, we do confirm that the key kinematic properties (Figure 2 and Figure 3 as questioned) follow the same ranking order of directions as predicted.

We thank the reviewer for pointing out the apparent discrepancy between model simulation and observed data. We will elaborate on the reasons behind the discrepancy in the revision.

Then, to strengthen the conclusions, I feel that the following points would need to be addressed:

(1) The authors model the movement control through equations that derive the input control variable in terms of the force acting on the hand and treat the arm as a second-order low-pass filter (Equation 13). Underestimation of the mass in the computation of a feedforward command would lead to a lower-than-expected displacement to that command. But it is not clear if and how the authors account for a potential modification of the time constants of the 2nd order system. The CNS does not effectuate movements with pure torque generators. Muscles have elastic properties that depend on their tonic excitation level, reflex feedback, and other parameters. Indeed, Fisk et al.* showed variations of movement characteristics consistent with lower muscle tone, lower bandwidth, and lower damping ratio in 0g compared to 1g. Could the variations in the response to the initial feedforward command be explained by a misrepresentation of the limbs' damping and natural frequency, leading to greater uncertainty about the consequences of the initial command? This would still be an argument for unadapted feedforward control of the movement, leading to the need for more corrective movements. But it would not necessarily reflect an underestimation of body mass.

*Fisk, J. O. H. N., Lackner, J. R., & DiZio, P. A. U. L. (1993). Gravitoinertial force level influences arm movement control. Journal of neurophysiology, 69(2), 504-511.

We agree that muscle properties, tonic excitation level, proprioception-mediated reflexes all contribute to reaching control. Fisk et al. (1993) study indeed showed that arm movement kinematics change, possibly owing to lower muscle tone and/or damping. However, reduced muscle damping and reduced spindle activity are more likely to affect feedback-based movements. Like in Fisk et al.’s study, people performed continuous arm movements with eyes closed; thus their movements largely relied on proprioceptive control. Our major findings are about the feedforward control, i.e., the reduced and “advanced” peak velocity/acceleration in discrete and ballistic reaching movements. Note that the peak acceleration happens as early as approximately 90-100ms into the movements, clearly showing that feedforward control is affected -- a different effect from Fisk et al’s findings. It is unlikely that people “advanced” their peak velocity/acceleration because they feel the need for more later corrective movements. Thus, underestimation of body mass remains the most plausible explanation.

(2) The movements were measured by having the subjects slide their finger on the surface of a touch screen. In weightlessness, the implications of this contact are expected to be quite different than those on the ground. In weightlessness, the taikonauts would need to actively press downward to maintain contact with the screen, while on Earth, gravity will do the work. The tangential forces that resist movement due to friction might therefore be different in 0g. This could be particularly relevant given that the effect of friction would interact with the limb in a direction-dependent fashion, given the anisotropy of the equivalent mass at the fingertip evoked by the authors. Is there some way to discount or control for these potential effects?

We agree that friction might play a role here, but normal interaction with a touch screen typically involves friction between 0.1 and 0.5N (e.g., Ayyildiz et al., 2018). We believe that the directional variation is even smaller than 0.1N. It is very small compared to the force used to accelerate the arm for the reaching movement (10-15N). Thus, friction anisotropy is unlikely to explain our data.

Citation: Ayyildiz M, Scaraggi M, Sirin O, Basdogan C, Persson BNJ. Contact mechanics between the human finger and a touchscreen under electroadhesion. Proc Natl Acad Sci U S A. 2018 Dec 11;115(50):12668-12673.

(3) The carefully crafted modelling of the limb neglects, nevertheless, the potential instability of the base of the arm. While the taikonauts were able to use their left arm to stabilize their bodies, it is not clear to what extent active stabilization with the contralateral limb can reproduce the stability of the human body seated in a chair in Earth gravity. Unintended motion of the shoulder could account for a smaller-than-expected displacement of the hand in response to the initial feedforward command and/or greater propensity for errors (with a greater need for corrective submovements) in 0g. The direction of movement with respect to the anchoring point could lead to the dependence of the observed effects on movement direction. Could this be tested in some way, e.g., by testing subjects on the ground while standing on an unstable base of support or sitting on a swing, with the same requirement to stabilize the torso using the contralateral arm?

Body stabilization is always a challenge for human movement studies in space. We minimized its potential confounding effects by using left-hand grasping and foot straps for postural support throughout the experiment. We would argue shoulder stability is an unlikely explanation because unexpected shoulder instability should not affect the feedforward (early) part of the ballistic reaching movement: the reduced peak acceleration and its early peak were observed at about 90-100ms after movement initiation. This effect is too early to be explained by an expected stability issue.

The arguments for an underestimation of body mass would be strengthened if the authors could address these points in some way.

Author Response

Reviewer #1 (Public Review):

[...] Genes expressed in the same direction in lowland individuals facing hypoxia (the plastic state) as what is found in the colonised state are defined as adaptative, while genes with the opposite expression pattern were labelled as maladaptive, using the assumption that the colonised state must represent the result of natural selection. Furthermore, genes could be classified as representing reversion plasticity when the expression pattern differed between the plasticity and colonised states and as reinforcement when they were in the same direction (for example more expressed in the plastic state and the colonised state than in the ancestral state). They found that more genes had a plastic expression pattern that was labelled as maladaptive than adaptive. Therefore, some of the genes have an expression pattern in accordance with what would be predicted based on the plasticity-first hypothesis, while others do not.

Thank you for a precise summary of our work. We appreciate the very encouraging comments recognizing the value of our work. We have addressed concerns from the reviewer in greater detail below.

Q1. As pointed out by the authors themselves, the fact that temperature was not included as a variable, which would make the experimental design much more complex, misses the opportunity to more accurately reflect the environmental conditions that the colonizer individuals face at high altitude. Also pointed out by the authors, the acclimation experiment in hypoxia lasted 4 weeks. It is possible that longer term effects would be identifiable in gene expression in the lowland individuals facing hypoxia on a longer time scale. Furthermore, a sample size of 3 or 4 individuals per group depending on the tissue for wild individuals may miss some of the natural variation present in these populations. Stating that they have a n=7 for the plastic stage and n= 14 for the ancestral and colonized stages refers to the total number of tissue samples and not the number of individuals, according to supplementary table 1.

We shared the same concerns as the reviewer. This is partly because it is quite challenging to bring wild birds into captivity to conduct the hypoxia acclimation experiments. We had to work hard to perform acclimation experiments by taking lowland sparrows in a hypoxic condition for a month. We indeed have recognized the similar set of limitations as the review pointed out and have discussed the limitations in the study, i.e., considering hypoxic condition alone, short time acclimation period, etc. Regarding sample sizes, we have collected cardiac muscle from nine individuals (three individuals for each stage) and flight muscle from 12 individuals (four individuals for each stage). We have clarified this in Supplementary Table 1.

Q2. Finally, I could not find a statement indicating that the lowland individuals placed in hypoxia (plastic stage) were from the same population as the lowland individuals for which transcriptomic data was already available, used as the "ancestral state" group (which themselves seem to come from 3 populations Qinghuangdao, Beijing, and Tianjin, according to supplementary table 2) nor if they were sampled in the same time of year (pre reproduction, during breeding, after, or if they were juveniles, proportion of males or females, etc). These two aspects could affect both gene expression (through neutral or adaptive genetic variation among lowland populations that can affect gene expression, or environmental effects other than hypoxia that differ in these populations' environments or because of their sexes or age). This could potentially also affect the FST analysis done by the authors, which they use to claim that strong selective pressure acted on the expression level of some of the genes in the colonised group.

The reviewer asked how individual tree sparrows used in the transcriptomic analyses were collected. The individuals used for the hypoxia acclimation experiment and represented the ancestral lowland population were collected from the same locality (Beijing) and at the same season (i.e., pre-breeding) of the year. They are all adults and weight approximately 18g. We have clarified this in the Supplementary Table S1 and Methods. We did not distinguish males from females (both sexes look similar) under the assumption that both sexes respond similarly to hypoxia acclimation in their cardiac and flight muscle gene expression.

The Supplementary Table 2 lists the individuals that were used for sequence analyses. These individuals were only used for sequence comparisons but not for the transcriptomic analyses. The population genetic structure analyzed in a previously published study showed that there is no clear genetic divergence within the lowland population (i.e., individuals collected from Beijing, Tianjing and Qinhuangdao) or the highland population (i.e., Gangcha and Qinghai Lake). In addition, there was no clear genetic divergence between the highland and lowland populations (Qu et al. 2020).

Author response image 1.

Population genetic structure of the Eurasian Tree Sparrow (Passer montanus). The genetic structure generated using FRAPPE. The colors in each column represent the contribution from each subcluster (Qu et al. 2020). Yellow, highland population; blue, lowland population.

Q4. Impact of the work There has been work showing that populations adapted to high altitude environments show changes in their hypoxia response that differs from the short-term acclimation response of lowland population of the same species. For example, in humans, see Erzurum et al. 2007 and Peng et al. 2017, where they show that the hypoxia response cascade, which starts with the gene HIF (Hypoxia-Inducible Factor) and includes the EPO gene, which codes for erythropoietin, which in turns activates the production of red blood cell, is LESS activated in high altitude individuals compared to the activation level in lowland individuals (which gives it its name). The present work adds to this body of knowledge showing that the short-term response to hypoxia and the long term one can affect different pathways and that acclimation/plasticity does not always predict what physiological traits will evolve in populations that colonize these environments over many generations and additional selection pressure (UV exposure, temperature, nutrient availability). Altogether, this work provides new information on the evolution of reaction norms of genes associated with the physiological response to one of the main environmental variables that affects almost all animals, oxygen availability. It also provides an interesting model system to study this type of question further in a natural population of homeotherms.

Erzurum, S. C., S. Ghosh, A. J. Janocha, W. Xu, S. Bauer, N. S. Bryan, J. Tejero et al. "Higher blood flow and circulating NO products offset high-altitude hypoxia among Tibetans." Proceedings of the National Academy of Sciences 104, no. 45 (2007): 17593-17598. Peng, Y., C. Cui, Y. He, Ouzhuluobu, H. Zhang, D. Yang, Q. Zhang, Bianbazhuoma, L. Yang, Y. He, et al. 2017. Down-regulation of EPAS1 transcription and genetic adaptation of Tibetans to high-altitude hypoxia. Molecular biology and evolution 34:818-830.

Thank you for highlighting the potential novelty of our work in light of the big field. We found it very interesting to discuss our results (from a bird species) together with similar findings from humans. In the revised version of manuscript, we have discussed short-term acclimation response and long-term adaptive evolution to a high-elevation environment, as well as how our work provides understanding of the relative roles of short-term plasticity and long-term adaptation. We appreciate the two important work pointed out by the reviewer and we have also cited them in the revised version of manuscript.

Reviewer #2 (Public Review):

This is a well-written paper using gene expression in tree sparrow as model traits to distinguish between genetic effects that either reinforce or reverse initial plastic response to environmental changes. Tree sparrow tissues (cardiac and flight muscle) collected in lowland populations subject to hypoxia treatment were profiled for gene expression and compared with previously collected data in 1) highland birds; 2) lowland birds under normal condition to test for differences in directions of changes between initial plastic response and subsequent colonized response. The question is an important and interesting one but I have several major concerns on experimental design and interpretations.

Thank you for a precise summary of our work and constructive comments to improve this study. We have addressed your concerns in greater detail below.

Q1. The datasets consist of two sources of data. The hypoxia treated birds collected from the current study and highland and lowland birds in their respective native environment from a previous study. This creates a complete confounding between the hypoxia treatment and experimental batches that it is impossible to draw any conclusions. The sample size is relatively small. Basically correlation among tens of thousands of genes was computed based on merely 12 or 9 samples.

We appreciate the critical comments from the reviewer. The reviewer raised the concerns about the batch effect from birds collected from the previous study and this study. There is an important detail we didn’t describe in the previous version. All tissues from hypoxia acclimated birds and highland and lowland birds have been collected at the same time (i.e., Qu et al. 2020). RNA library construction and sequencing of these samples were also conducted at the same time, although only the transcriptomic data of lowland and highland tree sparrows were included in Qu et al. (2020). The data from acclimated birds have not been published before.

In the revised version of manuscript, we also compared log-transformed transcript per million (TPM) across all genes and determined the most conserved genes (i.e., coefficient of variance ≤  0.3 and average TPM ≥ 1 for each sample) for the flight and cardiac muscles, respectively (Hao et al. 2023). We compared the median expression levels of these conserved genes and found no difference among the lowland, hypoxia-exposed lowland, and highland tree sparrows (Wilcoxon signed-rank test, P<0.05). As these results suggested little batch effect on the transcriptomic data, we used TPM values to calculate gene expression level and intensity. This methodological detail has been further clarified in the Methods and we also provided a new supplementary Figure (Figure S5) to show the comparative results.

Author response image 2.

The median expression levels of the conserved genes (i.e., coefficient of variance ≤ 0.3 and average TPM ≥ 1 for each sample) did not differ among the lowland, hypoxia-exposed lowland, and highland tree sparrows (Wilcoxon signed-rank test, P<0.05).

The reviewer also raised the issue of sample size. We certainly would have liked to have more individuals in the study, but this was not possible due to the logistical problem of keeping wild bird in a common garden experiment for a long time. We have acknowledged this in the manuscript. In order to mitigate this we have tested the hypothesis of plasticity following by genetic change using two different tissues (cardiac and flight muscles) and two different datasets (co-expressed gene-set and muscle-associated gene-set). As all these analyses show similar results, they indicate that the main conclusion drawn from this study is robust.

Q2. Genes are classified into two classes (reversion and reinforcement) based on arbitrarily chosen thresholds. More "reversion" genes are found and this was taken as evidence reversal is more prominent. However, a trivial explanation is that genes must be expressed within a certain range and those plastic changes simply have more space to reverse direction rather than having any biological reason to do so.

Thank you for the critical comments. There are two questions raised we should like to address them separately. The first concern centered on the issue of arbitrarily chosen thresholds. In our manuscript, we used a range of thresholds, i.e., 50%, 100%, 150% and 200% of change in the gene expression levels of the ancestral lowland tree sparrow to detect genes with reinforcement and reversion plasticity. By this design we wanted to explore the magnitudes of gene expression plasticity (i.e., Ho & Zhang 2018), and whether strength of selection (i.e., genetic variation) changes with the magnitude of gene expression plasticity (i.e., Campbell-Staton et al. 2021).

As the reviewer pointed out, we have now realized that this threshold selection is arbitrarily. We have thus implemented two other categorization schemes to test the robustness of the observation of unequal proportions of genes with reinforcement and reversion plasticity. Specifically, we used a parametric bootstrap procedure as described in Ho & Zhang (2019), which aimed to identify genes resulting from genuine differences rather than random sampling errors. Bootstrap results suggested that genes exhibiting reversing plasticity significantly outnumber those exhibiting reinforcing plasticity, suggesting that our inference of an excess of genes with reversion plasticity is robust to random sampling errors. We have added these analyses to the revised version of manuscript, and provided results in the Figure 2d and Figure 3d.

Author response image 3.

Figure 2a (left) and Figure 2b (right). Frequencies of genes with reinforcement and reversion plasticity (>50%) and their subsets that acquire strong support in the parametric bootstrap analyses (≥ 950/1000).

In addition, we adapted a bin scheme (i.e., 20%, 40% and 60% bin settings along the spectrum of the reinforcement/reversion plasticity). These analyses based on different categorization schemes revealed similar results, and suggested that our inference of an excess of genes with reversion plasticity is robust. We have provided these results in the Supplementary Figure S2 and S4.

Author response image 4.

(A) and Figure S4 (B). Frequencies of genes with reinforcement and reversion plasticity in the flight and cardiac muscle. (A) For genes identified by WGCNA, all comparisons show that there are more genes showing reversion plasticity than those showing reinforcement plasticity for both the flight and cardiac msucles. (B) For genes that associated with muscle phentoypes, all comparisons show that there are more genes showing reversion plasticity than those showing reinforcement plasticity for the flight muscle, while more than 50% of comparisons support an excess of genes with reversion plasticity for the cardiac muscle. Two-tailed binomial test, NS, non-significant; , P < 0.05; , P < 0.01; **, P < 0.001.

The second issue that the reviewer raised is that the plastic changes simply have more space to reverse direction rather than having any biological reason to do so. While a causal reason why there are more genes with expression levels being reversed than those with expression levels being reinforced at the late stages is still contentious, increasingly many studies show that genes expression plasticity at the early stage may be functionally maladapted to novel environment that the species have recently colonized (i.e., lizard, Campbell-Staton et al. 2021; Escherichia coli, yeast, guppies, chickens and babblers, Ho and Zhang 2018; Ho et al. 2020; Kuo et al. 2023). Our comparisons based on the two genesets that are associated with muscle phenotypes corroborated with these previous studies and showed that initial gene expression plasticity may be nonadaptive to the novel environments (i.e., Ghalambor et al. 2015; Ho & Zhang 2018; Ho et al. 2020; Kuo et al. 2023; Campbell-Staton et al. 2021).

Q3. The correlation between plastic change and evolved divergence is an artifact due to the definitions of adaptive versus maladaptive changes. For example, the definition of adaptive changes requires that plastic change and evolved divergence are in the same direction (Figure 3a), so the positive correlation was a result of this selection (Figure 3d).

The reviewer raised an issue that the correlation between plastic change and evolved divergence is an artifact because of the definition of adaptive versus maladaptive changes, for example, Figure 3d. We agree with the reviewer that the correlation analysis is circular because the definition of adaptive and maladaptive plasticity depends on the direction of plastic change matched or opposed that of the colonized tree sparrows. We have thus removed previous Figure 3d-e and related texts from the revised version of manuscript. Meanwhile, we have changed Figure 3a to further clarify the schematic framework.

Author response:

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

Reviewer #1 (Public Review):

Summary: 

The idea is appealing, but the authors have not sufficiently demonstrated the utility of this approach.

Strengths: 

Novelty of the approach, potential impli=cations for discovering novel interactions

Weaknesses:

The Duong had introduced their highly elegant peptidisc approach several years ago. In this present work, they combine it with thermal proteome profiling (TPP) and attempt to demonstrate the utility of this combination for identifying novel membrane protein-ligand interactions.

While I find this idea intriguing, and the approach potentially useful, I do not feel that the authors had sufficiently demonstrated the utility of this approach. My main concern is that no novel interactions are identified and validated. For the presentation of any new methodology, I think this is quite necessary. In addition, except for MsbA, no orthogonal methods are used to support the conclusions, and the authors rely entirely on quantifying rather small differences in abundances using either iBAQ or LFQ.

We thank the reviewer for their thoughtful comments. In this revision, we have experimentally addressed the reviewer’s concerns in three ways:

(1) To demonstrate the utility of our MM-TPP method over the detergent-based TPP workflow (termed DB-TPP), we performed a side-by-side comparison using ATP–VO₄ at 51 °C (Figure 3B and Figure 4A). From the DB-TPP dataset, 7.4% of all identified proteins were annotated as ATP-binding, while 6.4% of proteins differentially stabilized were annotated as ATP-binding. In contrast, in the MM-TPP dataset, 9.3% of all identified proteins were annotated as ATP-binding proteins, while 17% of proteins differentially stabilized were annotated as ATP-binding. The lack of enrichment in the detergent-based approach indicates that the observed differences are likely stochastic, rather than a result of specific ATP–VO₄-mediated stabilization as found with MM-TPP. For instance, several key proteins—BCS1, P2RY6, SLC27A2, ABCB1, ABCC2, and ABCC9— found differentially stabilized using the MM-TPP method showed no such pattern in the DB-TPP dataset. This divergence strongly supports the specificity and utility of our Peptidisc approach. 

(2) To demonstrate that MM-TPP can resolve not only the broader effects of ATP–VO₄ but also specific ligand–protein interactions, we employed 2-methylthio-ADP (2-MeS-ADP), a selective agonist of the P2RY12 receptor [PMID: 24784220]. In that case, we observed clear thermal stabilization of P2RY12, with more than 6-fold increase in stability at both 51 °C and 57 °C (–log₁₀ p > 5.97; Figure 4B and Figure S4). Notably, no other proteins—including the structurally related but non-responsive P2RY6 receptor- showed comparable stabilization fold change at these temperatures.

(3) To further probe the reproducibility of the method, we performed an independent MMTPP evaluation with ATP–VO₄ at 51 °C using data-independent acquisition (DIA), in contrast to the data-dependent acquisition (DDA) approach used in the initial study (Figure S5). Overall, 7.8% of all identified proteins were annotated as ATP-binding, and as before, this proportion increased to 17% among proteins with log₂ fold changes greater than 0.5. Specifically, BCS1 and SLC27A2 exhibited strong stabilization (log₂ fold change > 1), while P2RY6, ABCB11, ABCC2, and ABCG2 showed moderate stabilization (log₂ fold changes between 0.5 and 1), and consistent with previous results, P2RX4 was destabilized, with a log₂ fold change below –1. These findings support the consistency and reproducibility of the method across distinct data acquisition methods.

My main concern is that no novel interactions are identified and validated. For the presentation of any new methodology, I think this is quite necessary.  

The primary objective of our study is to establish and benchmark the MM-TPP workflow using known targets, rather than to discover novel ligand–protein interactions. Identifying new binders requires extensive screening and downstream validations, which we believe is beyond the scope of this methodological report. Instead, our study highlights the sensitivity and reliability of the MM-TPP approach by demonstrating consistent and reproducible results with well-characterized interactions.

We respectfully disagree with the notion that introducing a new methodology must necessarily include the discovery of novel interactions. For instance, Martinez Molina et al. [PMID: 23828940] introduced the cellular thermal shift assay (CETSA) by validating established targets such as MetAP2 with TNP-470 and CDK2 with AZD-5438, without identifying novel protein–ligand pairs. Similarly, Kalxdorf et al. [PMID: 33398190] published their cell-surface thermal proteome profiling (CS-TPP) using Ouabain to stabilize the Na⁺/K⁺-ATPase pump in K562 cells, and SB431542 to stabilize its canonical target JAG1. In fact, when these methods revealed additional stabilizations, these were not validated but instead interpreted through reasoning grounded in the literature. For instance, they attributed the SB431542-induced stabilization of MCT1 to its reported role in cell migration and tumor invasiveness, and explained that SLC1A2 stabilization is related to the disruption of Na⁺/K⁺-ATPase activity by Ouabain. In the same way, our interpretation of ATP-VO₄–mediated stabilization of Mao-B is justified by predictive AlphaFold-3 rather than direct orthogonal assays, which are beyond the scope of our methodological presentation. 

Collectively, the influential studies cited above have set methodological precedents by prioritizing validation and proof-of-concept over merely finding uncharacterized binders. In the same spirit, our work is centred on establishing MM-TPP as a robust platform for probing membrane protein–ligand interactions in a water-soluble format. The discovery of novel binders remains an exciting future direction—one that will build upon the methodological foundation laid by the present study.

In addition, except for MsbA, no orthogonal methods are used to support the conclusions, and the authors rely entirely on quantifying rather small differences in abundances using either iBAQ or LFQ.

We deliberately began this study with our model protein, MsbA, examined under both native and overexpressed conditions, to establish an adequation between MMTPP (Figure 2D) and biochemical stability assays (Figure 2A). This validation has provided us with the foundation to confidently extend MM-TPP to the mouse organ proteome. To demonstrate the validity of our workflow, we have used ATP-VO₄ because it has expected targets. 

We note that orthogonal validation often requires overproduction and purification of the candidate proteins, including suitable antibodies, which is a true challenge for membrane proteins. Here, we demonstrate that MM-TPP can detect ligand-induced thermal shifts directly in native membrane preparations, without requiring protein overproduction or purification. We also emphasize several influential studies in TPP, including Martinez Molina et al. (PMID: 23828940) and Fang et al. (PMID: 34188175), which focused primarily on establishing and benchmarking the methodology, rather than on extensive orthogonal validation. In the same spirit, our study prioritizes methodological development, and accordingly, several orthogonal validations are now included in this revision.

[...] and the authors rely entirely on quantifying rather small differences in abundances using either iBAQ or LFQ.

To clarify, all analyses on ligand-induced stabilization or destabilization were carried out using LFQ values. The sole exception is on Figure 2B, where we used iBAQ values to depict the relative abundance of proteins within a single sample; this to show MsbA's relative level within the E. coli peptidisc library.

Respectfully, we disagree with the assertion that we are “quantifying rather small differences in abundances using either iBAQ or LFQ.” We were able to clearly distinguish between stabilizations driven by specific ligands binding to their targets versus those caused by non-specific ligands with broader activity. This is further confirmed by comparing 2-MeS-ADP, a selective ligand for P2RY12, with ATP-VO₄, a highly promiscuous ligand, and AMP-PNP, which exhibits intermediate breadth. When tested in triplicate at 51 °C, 2-MeS-ADP significantly altered the thermal stability of 27 proteins,  AMP-PNP 44 proteins, and ATP-VO₄ 230 proteins, consistent with the expectation that broader ligands stabilize more proteins nonspecifically. Importantly, 2-MeS-ADP produced markedly stronger stabilization of its intended target, P2RY12 (–log₁₀p = 9.32), than the top stabilized proteins for ATP–VO₄ (DNAJB3, –log₁₀p = 5.87) or AMP-PNP (FTH1, p = 5.34). Moreover, 2-MeS-ADP did not significantly stabilize proteins that were consistently stabilized by the broad ligands, such as SLC27A2, which was strongly stabilized by both ATP-VO₄ and AMP-PNP (–log₁₀ p>2.5). Together, these findings demonstrate that MMTPP can robustly distinguish between broad-spectrum and target-specific ligands, with selective ligands inducing stronger and more physiologically meaningful stabilization at their intended targets compared to promiscuous ligands.

Finally, we emphasize that our findings are not marginal, but meet quantitative and statistical rigor consistent with best practices in proteomics. We apply dual thresholds combining effect size (|log₂FC| ≥ 1, i.e., at least a two-fold change) with statistical significance (FDR-adjusted p ≤ 0.05)—criteria commonly used in proteomics methodology studies (e.g., PMID: 24942700, 38724498). Moreover, the stabilization and destabilization events we report are reproducible across biological replicates (n = 3), consistent across adjacent temperatures for most targets, and technically robust across acquisition modes (DDA vs. DIA). Taken together, these results reflect statistically valid and biologically meaningful effects, fully aligned with standards set by prior published proteomics studies.

Furthermore, the reported changes in abundances are solely based on iBAQ or LFQ analysis. This must be supported by a more quantitative approach such as SILAC or labeled peptides. In summary, I think this story requires a stronger and broader demonstration of the ability of peptidisc-TPP to identify novel physiologically/pharmacologically relevant interactions.

With respect to labeling strategies, we deliberately avoided using TMT due to concerns about both cost and potential data quality issues. Some recent studies have documented the drawbacks of TMT in contexts directly relevant to our work. For example, a benchmarking study of LiP-MS workflows showed that although TMT increased proteome depth and reduced technical variance, it was less accurate in identifying true drug–protein interactions and produced weaker dose–response correlations compared with label-free DIA approaches [PMID: 40089063]. More broadly, technical reviews have highlighted that isobaric tagging is intrinsically prone to ratio compression and reporterion interference due to co-isolation and co-fragmentation of peptides, which flatten measured fold-changes and obscure biologically meaningful differences [PMID: 22580419, 22036744]. In terms of SILAC, the technique requires metabolic incorporation of heavy amino acids, which is feasible in cultured cells but not in physiologically relevant tissues such as the liver organ used here. SILAC mouse models exist, but they are expensive and time-consuming [PMID: 18662549, 21909926]. We are not a mouse lab, and introducing liver organ SILAC labeling in our workflow is beyond the scope of these revisions. We also note that several hallmark TPP studies have been successfully carried out using label-free quantification [PMID: 25278616, 26379230, 33398190, 23828940], establishing this as an accepted and widely applied approach in the field. 

To further support our conclusions, we added controls showing that detergent solubilization of mouse liver membranes followed by SP4 cleanup fails to detect ATP-VO₄– mediated stabilization of ATP-binding proteins, underscoring the necessity of Peptidisc reconstitution for capturing ligand-induced thermal stabilization. We also present new data demonstrating selective stabilization of the P2Y12 receptor by its agonist 2-MeS-ADP, providing orthogonal, receptor-specific validation within the MM-TPP framework. Finally, an orthogonal DIA acquisition on separate replicates confirmed robust ATP-vanadate stabilization of ATP-binding proteins, including BCS1l and SLC27A2. Together, these additions reinforce that the observed stabilizations are genuine, physiologically relevant ligand–protein interactions and highlight the unique advantage of the Peptidisc-based workflow in capturing such events.

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Reviewer #2 (Public Review):

Summary:

The membrane mimetic thermal proteome profiling (MM-TPP) presented by Jandu et al. seems to be a useful way to minimize the interference of detergents in efficient mass spectrometry analysis of membrane proteins. Thermal proteome profiling is a mass spectrometric method that measures binding of a drug to different proteins in a cell lysate by monitoring thermal stabilization of the proteins because of the interaction with the ligands that are being studied. This method has been underexplored for membrane proteome because of the inefficient mass spectrometric detection of membrane proteins and because of the interference from detergents that are used often for membrane protein solubilization.

Strengths:

In this report the binding of ligands to membrane protein targets has been monitored in crude membrane lysates or tissue homogenates exalting the efficacy of the method to detect both intended and off-target binding events in a complex physiologically relevant sample setting.

The manuscript is lucidly written and the data presented seems clear. The only insignificant grammatical error I found was that the 'P' in the word peptidisc is not capitalized in the beginning of the methods section "MM-TPP profiling on membrane proteomes". The clear writing made it easy to understand and evaluate what has been presented. Kudos to the authors.

Weaknesses:

While this is a solid report and a promising tool for analyzing membrane protein drug interactions, addressing some of the minor caveats listed below could make it much more impactful.

The authors claim that MM-TPP is done by "completely circumventing structural perturbations invoked by detergents[1] ". This may not be entirely accurate, because before reconstitution of the membrane proteins in peptidisc, the membrane fractions are solubilized by 1% DDM. The solubilization and following centrifugation step lasts at least for 45 min. It is less likely that all the structural perturbations caused by DDM to various membrane proteins and their transient interactions become completely reversed or rescued by peptidisc reconstitution.

We thank the reviewer for this insightful comment. In response, we have revised the sentence and expanded the discussion to clarify that the Peptidisc provides a complementary approach to detergent-based preparations for studying membrane proteins, preserving native lipid–protein interactions and stabilization effects that may be diminished in detergent.

To further address the structural perturbations invoked by detergents, and as already detailed to our response to Reviewer 1, we have compared the thermal profile of the Peptidisc library to the mouse liver membranes solubilized with 1% DDM, after incubation with ATP–VO₄ at 51 °C (Figure 4A). The results with the detergent extract revealed random patterns of stabilization and destabilization, with only 6.4% of differentially stabilized proteins being ATP-binding—comparable to the 7.4% observed in the background. In contrast, in the Peptidisc library, 17% of differentially stabilized proteins were ATP-binding, compared to 9.3% in the background. Thus, while Peptidisc reconstitution does not fully avoid initial detergent exposure, these findings underscore the importance of implementing Peptidisc in the TPP workflow when dealing with membrane proteins.

In the introduction, the authors make statements such as "..it is widely acknowledged that even mild detergents can disrupt protein structures and activities, leading to challenges in accurately identifying drug targets.." and "[peptidisc] libraries are instrumental in capturing and stabilizing IMPs in their functional states while preserving their interactomes and lipid allosteric modulators...'. These need to be rephrased, as it has been shown by countless studies that even with membrane protein suspended in micelles robust ligand binding assays and binding kinetics have been performed leading to physiologically relevant conclusions and identification of protein-protein and protein-ligand interactions.

We thank the reviewer for this valuable feedback and fully agree with the point raised. In response, we have revised the Introduction and conclusion to moderate the language concerning the limitations of detergent use. We now explicitly acknowledge that numerous studies have successfully used detergent micelles for ligand-binding assays and kinetic analyses, yielding physiologically relevant insights into both protein–protein and protein–ligand interactions [e.g., PMID: 22004748, 26440106, 31776188].

At the same time, we clarify that the Peptidisc method offers a complementary advantage, particularly in the context of thermal proteome profiling (TPP), which involves mass spectrometry workflows that are incompatible with detergents. In this setting, Peptidiscs facilitate the detection of ligand-binding events that may be more difficult to observe in detergent micelles.

We have reframed our discussion accordingly to present Peptidiscs not as a replacement for detergent-based methods, but rather as a complementary tool that broadens the available methodological landscape for studying membrane protein interactions.

If the method involves detergent solubilization, for example using 1% DDM, it is a bit disingenuous to argue that 'interactomes and lipid allosteric modulators' characterized by lowaffinity interactions will remain intact or can be rescued upon detergent removal. Authors should discuss this or at least highlight the primary caveat of the peptidisc method of membrane protein reconstitution - which is that it begins with detergent solubilization of the proteome and does not completely circumvent structural perturbations invoked by detergents.

We would like to clarify that, in our current workflow, ligand incubation occurs after reconstitution into Peptidiscs. As such, the method is designed to circumvent the negative effects of detergent during the critical steps involving low-affinity interactions.

That said, we fully acknowledge that Peptidisc reconstitution begins with detergent solubilization (e.g., 1% DDM), and we have revised the conclusion to explicitly state this important caveat. As the reviewer correctly points out, this initial step may introduce some structural perturbations or result in the loss of weakly associated lipid modulators.

However, reconstitution into Peptidiscs rapidly restores a detergent-free environment for membrane proteins, which has been shown in our previous studies [PMID: 38577106, 38232390, 31736482, 31364989] to mitigate these effects. Specifically, we have demonstrated that time-limited DDM exposure, followed by Peptidisc reconstitution, minimizes membrane protein delipidation, enhances thermal stability, retains functionality, and preserves multi-protein assemblies.

It would also be important to test detergents that are even milder than 1% DDM and ones which are harsher than 1% DDM to show that this method of reconstitution can indeed rescue the perturbations to the structure and interactions of the membrane protein done by detergents during solubilization step. 

We selected 1% DDM based on our previous work [PMID: 37295717, 39313981,38232390], where it consistently enabled robust and reproducible solubilization for Peptidisc reconstitution. We agree that comparing milder detergents (e.g., LMNG) and harsher ones (e.g., SDC) would provide valuable insights into how detergent strength influences structural perturbations, and how effectively these can be mitigated by Peptidisc reconstitution. Preliminary data (not shown) from mouse liver membranes indicate broadly similar proteomic profiles following solubilization with DDM, LMNG, and SDC, although potential differences in functional activity or ligand binding remain to be investigated.

Based on the methods provided, it appears that the final amount of detergent in peptidisc membrane protein library was 0.008%, which is ~150 uM. The CMC of DDM depending on the amount of NaCl could be between 120-170 uM.

While we cannot entirely rule out the presence of residual DDM (0.008%) in the raw library, its free concentration may be lower than initially estimated. This is related to the formation of mixed micelles with the amphipathic peptide scaffold, which is supplied in excess during reconstitution. These mixed micelles are subsequently removed during the ultrafiltration step. Furthermore, in related work using His-tagged Peptidiscs [PMID: 32364744], we purified the library by nickel-affinity chromatography following a 5× dilution into a detergent-free buffer. Although this purification step reduced the number of soluble proteins, the same membrane proteins were retained, suggesting that any residual detergent does not significantly interfere with Peptidisc reconstitution. Supporting this, our MM-TPP assays on purified libraries (data not shown) consistently demonstrated stabilization of ATP-binding proteins (e.g., SLC27A2, DNAJB3), indicating that the observed ligand–protein interactions result from successful incorporation into Peptidiscs.

Perhaps, to completely circumvent the perturbations from detergents other methods of detergentfree solubilization such as using SMA polymers and SMALP reconstitution could be explored for a comparison. Moreover, a comparison of the peptidisc reconstitution with detergent-free extraction strategies, such as SMA copolymers, could lend more strength to the presented method.

We agree that detergent-free methods such as SMA polymers hold promise for membrane protein solubilization. However, in preliminary single-replicate experiments using SMA2000 at 51 °C in the presence of ATP–VO₄ (data not shown), we observed broad, non-specific stabilization effects. Of the 2,287 quantified proteins, 9.3% were annotated as ATP-binding, yet 9.9% of the 101 proteins showing a log₂ fold change >1 or <–1 were ATPbinding, indicating no meaningful enrichment. Given this lack of specificity and the limited dataset, we chose not to pursue further SMA experiments and have not included them here. However, in a recent study (https://doi.org/10.1101/2025.08.25.672181), we directly compared Peptidisc, SMA, and nanodiscs for liver membrane proteome profiling. In that work, Peptidisc outperformed both SMA and nanodiscs in detecting membrane protein dysregulation between healthy and diseased liver. By extension, we expect Peptidisc to offer superior sensitivity and specificity for detecting ligand-induced stabilization events, such as those observed here with ATP–vanadate.

Cross-verification of the identified interactions, and subsequent stabilization or destabilizations, should be demonstrated by other in vitro methods of thermal stability and ligand binding analysis using purified protein to support the efficacy of the MM-TPP method. An example cross-verification using SDS-PAGE, of the well-studied MsbA, is shown in Figure 2. In a similar fashion, other discussed targets such as, BCS1L, P2RX4, DgkA, Mao-B, and some un-annotated IMPs shown in supplementary figure 3 that display substantial stabilization or destabilization should be cross-verified.

We appreciate this suggestion and note that a similar point was raised in R1’s comment “In addition, except for MsbA, no orthogonal methods are used to support the conclusions, and the authors rely entirely on quantifying rather small differences in abundances using either iBAQ or LFQ.” We have developed a detailed response to R1 on this matter, which equally applies here. 

Cited Reference:

35616533: Young JW, Wason IS, Zhao Z, et al. Development of a Method Combining Peptidiscs and Proteomics to Identify, Stabilize, and Purify a Detergent-Sensitive Membrane Protein Assembly. J Proteome Res. 2022;21(7):1748-1758. doi:10.1021/acs.jproteome.2c00129. PMID: 35616533.

31364989: Carlson ML, Stacey RG, Young JW, et al. Profiling the Escherichia coli membrane protein interactome captured in Peptidisc libraries. Elife. 2019;8:e46615. doi:10.7554/eLife.46615. 

22004748: O'Malley MA, Helgeson ME, Wagner NJ, Robinson AS. Toward rational design of protein detergent complexes: determinants of mixed micelles that are critical for the in vitro stabilization of a G-protein coupled receptor. Biophys J. 2011;101(8):1938-1948. doi:10.1016/j.bpj.2011.09.018.

26440106: Allison TM, Reading E, Liko I, Baldwin AJ, Laganowsky A, Robinson CV. Quantifying the stabilizing effects of protein-ligand interactions in the gas phase. Nat Commun. 2015;6:8551. doi:10.1038/ncomms9551.

31776188: Beckner RL, Zoubak L, Hines KG, Gawrisch K, Yeliseev AA. Probing thermostability of detergentsolubilized CB2 receptor by parallel G protein-activation and ligand-binding assays. J Biol Chem. 2020;295(1):181190. doi:10.1074/jbc.RA119.010696.

38577106: Jandu RS, Yu H, Zhao Z, Le HT, Kim S, Huan T, Duong van Hoa F. Capture of endogenous lipids in peptidiscs and effect on protein stability and activity. iScience. 2024;27(4):109382. doi:10.1016/j.isci.2024.109382.

38232390: Antony F, Brough Z, Zhao Z, Duong van Hoa F. Capture of the Mouse Organ Membrane Proteome Specificity in Peptidisc Libraries. J Proteome Res. 2024;23(2):857-867. doi:10.1021/acs.jproteome.3c00825.

31736482: Saville JW, Troman LA, Duong Van Hoa F. PeptiQuick, a one-step incorporation of membrane proteins into biotinylated peptidiscs for streamlined protein binding assays. J Vis Exp. 2019;(153). doi:10.3791/60661. 

37295717: Zhao Z, Khurana A, Antony F, et al. A Peptidisc-Based Survey of the Plasma Membrane Proteome of a Mammalian Cell. Mol Cell Proteomics. 2023;22(8):100588. doi:10.1016/j.mcpro.2023.100588. 

39313981: Antony F, Brough Z, Orangi M, Al-Seragi M, Aoki H, Babu M, Duong van Hoa F. Sensitive Profiling of Mouse Liver Membrane Proteome Dysregulation Following a High-Fat and Alcohol Diet Treatment. Proteomics. 2024;24(23-24):e202300599. doi:10.1002/pmic.202300599. 

32364744: Young JW, Wason IS, Zhao Z, Rattray DG, Foster LJ, Duong Van Hoa F. His-Tagged Peptidiscs Enable Affinity Purification of the Membrane Proteome for Downstream Mass Spectrometry Analysis. J Proteome Res. 2020;19(7):2553-2562. doi:10.1021/acs.jproteome.0c00022.

32591519: The M, Käll L. Focus on the spectra that matter by clustering of quantification data in shotgun proteomics. Nat Commun. 2020;11(1):3234. doi:10.1038/s41467-020-17037-3. 

33188197: Kurzawa N, Becher I, Sridharan S, et al. A computational method for detection of ligand-binding proteins from dose range thermal proteome profiles. Nat Commun. 2020;11(1):5783. doi:10.1038/s41467-02019529-8. 

26524241: Reinhard FBM, Eberhard D, Werner T, et al. Thermal proteome profiling monitors ligand interactions with cellular membrane proteins. Nat Methods. 2015;12(12):1129-1131. doi:10.1038/nmeth.3652. 

23828940: Martinez Molina D, Jafari R, Ignatushchenko M, et al. Monitoring drug target engagement in cells and tissues using the cellular thermal shift assay. Science. 2013;341(6141):84-87. doi:10.1126/science.1233606. 

32133759: Mateus A, Kurzawa N, Becher I, et al. Thermal proteome profiling for interrogating protein interactions. Mol Syst Biol. 2020;16(3):e9232. doi:10.15252/msb.20199232. 

14755328: Dorsam RT, Kunapuli SP. Central role of the P2Y12 receptor in platelet activation. J Clin Invest. 2004;113(3):340-345. doi:10.1172/JCI20986. 

Reviewer #1 (Recommendations for the authors):

“The authors use iBAC or LFQ to compare across samples. This inconsistency is puzzling. As far as I know, LFQ should always be used when comparing across samples”

As mentioned above, we use iBAQ only in Fig. 2B to illustrate within-sample relative abundance; all comparative analyses elsewhere use LFQ. We have updated the Fig. 2B legend to state this explicitly.

We used iBAQ Fig. 2B as it provides a notion of protein abundance within a sample, normalizing the summed peptide intensities by the number of theoretically observable peptides. This normalization facilitates comparisons between proteins within the same sample, offering a clearer understanding of their relative molar proportions [PMID: 33452728]. LFQ, by contrast, is optimized for comparing the same protein across different samples. It achieves this by performing delayed normalization to reduce run-to-run variability and by applying maximal peptide ratio extraction, which integrates pairwise peptide intensity ratios across all samples to build a consistent protein-level quantification matrix [PMID: 24942700]. These features make LFQ more robust to missing values and technical variation, thereby enabling accurate detection of relative abundance changes in the same protein under different experimental conditions. This distinction is well supported by the proteomics literature: Smits et al. [PMID: 23066101] used iBAQ specifically to determine the relative abundance of proteins within one sample, whereas LFQ was applied for comparative analyses between conditions.

“[Regarding Figure 2A] Why does the control also contain ATP-vanadate? Also, I am not aware of a commercially available chemical "ATP-VO4". I assume this is a mistake”

The control condition in Figure 2A was mislabeled, and the figure has been corrected to remove this discrepancy. In our experiments, ATP and orthovanadate (VO₄) were added together, and for simplicity this was annotated as “ATP-VO₄.” 

“[Regarding Figure 2B] What is the fold change in MsbA iBAQ values? It seems that the differences are quite small, and as such require a more quantitative approach than iBAQ (e.g SILAC or some other internal standard). In addition, what information does this panel add relative to 2C”

The figure has been updated to clarify that the values shown are log₂transformed iBAQ intensities. Figures 2B and 2C are complementary: Figure 2B shows that in the control sample, MsbA’s peptide abundance decreases with temperatures (51, 56, and 61 °C) relative to the remaining bulk proteins. Figure 2C shows the specific thermal profiles of MsbA in control and ATP–vanadate conditions. To make this clearer, we have added a sentence to the Results section explaining the specific role of Figure 2B.

Together, these panels indicate that the method can identify ligand-induced stabilization even for proteins whose abundance decreases faster than the bulk during the TPP assay. We have provided the rationale for not using SILAC or TMT labeling in our public response.

“[Regarding Figure 2C] Although not mentioned in the legend, I assume this is iBAQ quantification, which as mentioned above isn't accurate enough for such small differences. In addition, I find this data confusing: why is MsbA more stable at the lower temperatures in the absence of ATP-vanadate? The smoothed-line representation is misleading, certainly given the low number of data points”

The data presented represent LFQ values for MsbA, and we have updated the figure legend to clearly indicate this. Additionally, as suggested, we have removed the smoothing line to more accurately reflect the data. Regarding the reviewer’s concern about stability at lower temperatures, we note that MsbA exhibits comparable abundance at 38 °C and 46 °C under both conditions, with overlapping error bars. We therefore interpret these data as indicating no significant difference in stability at the lower temperatures, with ligand-dependent stabilization becoming apparent only at elevated temperatures. We do not exclude the possibility that MsbA stability at these temperatures is affected by the conformational dynamics of this ABC transporter upon ATP binding and hydrolysis.

“[Regarding Figure 3A] is this raw LFQ data? Why did the authors suddenly change from iBAQ to LFQ? I find this inconsistency puzzling”

To clarify, all analyses of protein stabilization or destabilization presented in the manuscript are based on LFQ values. The only instance where iBAQ was used is Figure 2B, where it served to illustrate the relative peptide abundance of MsbA within the same sample. We have revised the figure legends and text to make this distinction explicit and ensure consistency in presentation.

“[Regarding Figure 3B] The non-specific ATP-dependent stabilization increases the likelihood of false positive hits. This limitation is not mentioned by the authors. I think it is important to show other small molecules, in addition to ATP. The authors suggest that their approach is highly relevant for drug screening. Therefore, a good choice is to test an effect of a known stabilizing drug (eg VX-809 and CFTR)”

We thank the reviewer for this suggestion. As noted in the manuscript (results and discussion sections), ATP is a natural hydrotrope and is therefore expected to induce broad, non-specific stabilization effects, a phenomenon also observed in previous proteome-wide studies, which demonstrated ATP’s widespread influence on cytosolic protein solubility and thermal stability (PMID: 30858367). To demonstrate that MM-TPP can resolve specific ligand–protein interactions beyond these global ATP effects, we tested 2-methylthio-ADP (2-MeS-ADP), a selective agonist of P2RY12 (PMID: 14755328). In these experiments, we observed robust and reproducible stabilization of P2RY12 at both 51°C and 57°C, with no consistent stabilization of unrelated proteins across temperatures. This provides direct evidence that our workflow can distinguish specific from non-specific ligand-induced effects. We selected 2-MeS-ADP due to its structural stability and receptor higher-affinity over ADP, allowing us to extend our existing workflow while testing a receptor-specific interaction. We agree that extending this approach to clinically relevant small-molecule drugs, such as VX-809 with CFTR, would further underscore the pharmacological potential of MM-TPP, and we have now noted this as an important avenue for future studies.

“X axis of Figure 3B: Log 2 fold difference of what? iBAQ? LFQ? Similar ambiguity regarding the Y axis of 3E. What peptide? And why the constant changes in estimating abundances?”

We thank the reviewer for pointing out these inaccuracies in the figure annotations. As mentioned above, all analyses (except Figure 2B) are based on LFQ values. We have revised the figure legends and text to make this clear.

In Figure 3E, “peptide intensity” refers to log2 LFQ peptide intensities derived from the BCS1L protein, as indicated in the figure caption. 

“The authors suggest that P2RY6 and P2RY12 are stabilized by ADP, the hydrolysis product of ATP. Currently, the support for this suggestion is highly indirect. To support this claim, the authors need to directly show the effect of ADP. In reference to the alpha fold results shown in Figure 4D, the authors state that "Collectively, these data highlight the ability of MM-TPP to detect the side effects of parent compounds, an important consideration for drug development". To support this claim, it is necessary to show that Mao-B is indeed best stabilized with ADP or AMP, rather than ATP.”

In this revision, we chose not to test ADP directly, as it is a broadly binding, relatively weak ligand that would likely stabilize many proteins without revealing clear target-specific effects. Since we had already evaluated ATP-VO₄, a similarly broad, non-specific ligand, additional testing with ADP would provide limited additional insight. Instead, we prioritized 2-methylthio-ADP, a selective agonist of P2RY12, to more effectively demonstrate the specificity of MM-TPP. With this ligand, we observed clear and reproducible stabilization of P2RY12, underscoring the ability of MM-TPP to resolve receptor–ligand interactions beyond ATP’s broad hydrotropic effects. Importantly, and as expected, we did not observe stabilization of the related purinergic receptor P2RY6, further supporting the specificity of the observed effect.

We have also revised the AlphaFold-related statement in Figure 4D to adopt a more cautious tone: “Collectively, these data suggest that MM-TPP may detect potential side effects of parent compounds, an important consideration for drug development.” In this context, we use AlphaFold not as a validation tool, but rather as a structural aid to help rationalize why certain off-target proteins (e.g., ATP with Mao-B) exhibit stabilization.

Reviewer #2 (Recommendations for the authors):

“In the main text, it will be useful to include the unique peptides table of at least the targets discussed in the manuscript. For example, in presence of AMP-PNP at 51oC P2RY6 shows 4-6 peptides in all n=3 positive & negative ionization modes. But, for P2RY12 only 1-3 peptides were observed. Depending on the sequence length and the relative abundance in the cell of a protein of interest, the number of peptides observed could vary a lot per protein. Given the unique peptide abundance reported in the supplementary file, for various proteins in different conditions, it appears the threshold of observation of two unique peptides for a protein to be analyzed seems less stringent.”

By applying a filter requiring at least two unique peptides in at least one replicate, we exclude, on average, 15–20% of the total identified proteins. We consider this a reasonable level of stringency that balances confidence in protein identification with the retention of relevant data. This threshold was selected because it aligns with established LC-MS/MS data analysis practices (PMID: 32591519, 33188197, 26524241), and we have included these references in the Methods section to justify our approach. We have included in this revision a Supplemental Table 2 showing the unique peptide counts for proteins highlighted in this study.  

“It appears that the time of heat treatment for peptidisc library subjected to MM-TPP profiling was chosen as 3 min based on the results presented in Supplementary Figure 1A, especially the loss of MsbA observed in 1% DDM after 3 min heat perturbation. However, when reconstituted in peptidisc there seems to be no loss in MsbA even after 12 mins at 45oC. So, perhaps a longer heat treatment would be a more efficient perturbation.”

Previous studies indicate that heat exposure of 3–5 minutes is optimal for visualizing protein denaturation (PMID: 23828940, 32133759). We have added a statement to the Results section to justify our choice of heat exposure. Although MsbA remains stable at 45 °C for extended periods, higher temperatures allow for more effective perturbation to reveal destabilization. Supplementary Figure 1A specifically illustrates MsbA instability in detergent environments.

“Some of the stabilized temperatures listed in Table 1 are a bit confusing. For example, ABCC3 and ABCG2. In the case of ABCC3 stabilization was observed at 51oC and 60oC, but 56oC is not mentioned. In the same way, 51oC is not mentioned for ABCG2. You would expect protein to be stabilized at 56oC if it is stabilized at both 51oC and 60oC. So, it is unclear if the stabilizations were not monitored for these proteins at the missing temperatures in the table or if no peptides could be recorded at these temperatures as in the case of P2RX4 at 60oC in Figure 4C.”

Both scenarios are represented in our data. For some proteins, like ABCG2, sufficient peptide coverage was achieved, but no stabilization was observed at intermediate temperatures (e.g., 56 °C), likely because the perturbation was not strong enough to reveal an effect. In other cases, such as ABCC3 at 56 °C or P2RX4 at 60 °C, the proteins were not detected due to insufficient peptide identifications at those temperatures, which explains their omission from the table. 

“In Figure 4C, it is perplexing to note that despite n = 3 there were no peptide fragments detected for P2RX4 at 60oC in presence of ATP-VO4, but they were detected in presence of AMP-PNP. It will be useful to learn authors explanation for this, especially because both of these ligands destabilize P2RX4. In Figure 4B, it would have been great to see the effect of ADP too, to corroborate the theory that ATP metabolites could impact the thermal stability.”

In Figure 4C, the absence of P2RX4 peptide detection at 60 °C with ATP–VO₄ mirrors variability observed in the corresponding control (n = 6). Specifically, neither the control nor ATP–VO₄ produced unique peptides for P2RX4 at 60 °C in that replicate, whereas peptides were detected at 60 °C in other replicates for both the control and AMPPNP, and at 64 °C for ATP–VO₄, the controls, and AMP-PNP. Such missing values are a natural feature of MS-based proteomics and can arise from multiple technical factors, including inconsistent heating, incomplete digestion, stochastic MS injection, or interference from Peptidisc peptides. We therefore interpret the absence of peptides in this replicate as a technical artifact rather than evidence against protein destabilization. Importantly, the overall dataset consistently shows that both ATP–VO₄ and AMP-PNP destabilize P2RX4, supporting their characterization as broad, non-specific ligands with off-target effects.

Because ATP and ADP belong to the same class of broadly binding, non-specific ligands, additional testing with ADP would not provide meaningful mechanistic insight. Instead, we chose to test 2-methylthio-ADP, a selective P2RY12 agonist. This experiment revealed robust, reproducible stabilization of P2RY12, without consistent effects on unrelated proteins at 51 °C and 57 °C, thereby demonstrating the ability of MM-TPP to detect specific receptor–ligand interactions.

Finally, we note that P2RX4 is not a primary target of ATP–VO₄ or AMP-PNP. Consequently, the observed destabilization of P2RX4 is expected to be less pronounced than the strong, physiologically consistent stabilization of ABC transporters by ATP–VO₄, as shown in Figure 3D, where the majority of ABC transporters are thermally stabilized across all tested temperatures.

“As per Figure 4, P2Y receptors P2RY6 and P2RY12 both showed great thermal stability in presence of ATP-VO4 despite their preference for ADP. The authors argue this could be because of ATP metabolism, and binding of the resultant ADP to the P2RY6. If P2RX4 prefers ATP and not the metabolized product ADP that apparently is available, ideally you should not see a change in stability. A stark destabilization would indicate interaction of some sorts. P2X receptors are activated by ATP and are not naturally activated by AMP-PNP. So, destabilization of P2RX4 upon binding to ATP that can activate P2X receptors is conceivable. However, destabilization both in presence of ATP-VO4 and AMP-PNP is unclear. It is perhaps useful to test effect of ADP using this method, and maybe even compare some antagonists such as TNPATP.”

In this study, we did not directly test ADP, as we had already demonstrated that MM-TPP detects stabilization by broad-binding ligands such as ATP–VO₄. Instead, we focused on a more selective ligand, 2-MeS-ADP, a specific agonist of P2RY12 [PMID: 14755328]. Here, we observed robust and reproducible stabilization of P2RY12 at 51 °C and 57 °C, while P2RY6 showed no significant changes, and no other proteins were consistently stabilized (Figure 4B, S4). This confirms that MM-TPP can distinguish specific ligand–receptor interactions from broader ATP-induced effects. To further explore the assay’s nuance and sensitivity, testing additional nucleotide ligands—including antagonists like TNP-ATP or ATPγS—would provide valuable insights, and we have identified this as an important future direction.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Summary: This work by Matsui et al. examined the function of a gene Stand Stil (stil) in Drosophila in regulation of germ cell death in the female germline. They show that stil mutants contain many apoptotic cells, leading to germ cell loss and infertility. Gene expression analysis showed upregulation of pro-apoptotic genes such as rpr in stil mutant. DamID experiment further showed that stil binds to rpr promoter region to repress its expression. Additionally, they also show that undifferentiated germ cells are resistant to cell death in stil mutant (but stil mutant still eventually loses all germ cells).

Major comments: Overall, experiments adhere to a general standard of rigor, and each result is fairly convincing. In that sense, this paper warrants publication, as a paper that revealed a new gene important for preventing germ cell death. With that said, I feel that this paper does not reveal a new biological insight. In a nutshell, this paper is about a transcriptional repressor for pro-apoptotic gene, hence its depletion leads to cell death. Data is solid and the conclusion is well supported. But the readers will be left wondering why nature implemented such control? Unless one can show what kind of defects stil rpr double mutant (which rescues germ cell loss phenotype) exhibits, there is no insight why the balance of pro-apoptotic gene and its repressor is important. The paper discusses the 'molecular' mechanisms that explain the phenomenon, but it does not provide insights. The lack of conceptual advancement is the limitation of this work.

Response:

We thank the reviewer for pointing out a biological insight into the evolutionary rationale underlying the adoption of such a regulatory mechanism in nature. To address this point, we assessed the evolutionary conservation of rpr and stil through BLAST searches and comparative analyses. Our results showed that both genes are Diptera-restricted, whereas their key domains (the rpr IAP-binding motif and the Stil BED finger) are widely conserved across metazoans. In this phylogenetic context, we propose that Stil acts as a dedicated repressor of rpr in the Drosophila female germline, thereby establishing an apoptotic control architecture in which hid predominates and rpr is repressed by Stil. This explains why the balance between a potent effector (Rpr) and its repressor (Stil) is critical in oogenesis; preventing catastrophic germline loss while preserving hid-mediated responsiveness.

We have incorporated these phylogenetic analyses and the perspective into the revised Discussion section as follows.

Revised Page 22, Line 475; rpr is conserved only within Diptera, although its IAP-binding motif, essential for apoptosis induction, is broadly conserved across metazoans (Du et al., 2000; Gottfried et al., 2004; Hegde et al., 2002; Shi, 2002; Verhagen et al., 2000; Vucic et al., 1998; Wing et al., 2001; L. Zhou, 2005) (Fig. S7). Similarly, stil is also restricted to Diptera, predominantly within Drosophila, whereas its BED-type zinc finger domain is widely conserved among diverse organisms (Aravind, 2000; Hayward et al., 2013; Tue et al., 2017b; H. Zhou et al., 2016). Phylogenetic patterns across Diptera are consistent with a model in which stil acts as a dedicated repressor of rpr in the Drosophila germline cells (Fig. S7). Due to its potent pro-apoptotic activity, rpr must be stringently repressed in a spatiotemporal manner through mechanisms that are specific to both cell type and developmental stage. During embryogenesis, repression of rpr is mediated by the Dpp-signaling factor Shn, which binds to the rpr regulatory region, whereas in intestinal stem cells (ISCs), its expression is suppressed through chromatin conformation. In Drosophila female germline cells, hid serves as the primary regulator of apoptosis, while rpr activity is generally suppressed (Park et al., 2019; Xing et al., 2015). However, rpr mutants exhibit reduced fertility despite producing viable eggs (Fig. 3H), suggesting that rpr-mediated apoptosis may be required for proper egg development. Accordingly, we propose that stil restrains rpr in the Drosophila female germline, allowing hid to predominate in apoptotic regulation.

New Fig. S7;

The legend of new Fig. S7;

Figure S7 Conservation of Rpr and Stil within Diptera

Homologs of Drosophila melanogaster Rpr and Stil were identified by BLASTp, aligned, and analyzed phylogenetically. Homologs are present across Dipteran lineages, with the genus Drosophila highlighted in blue. Branch lengths indicate the expected number of substitutions per site, as shown by the scale bar.

Minor comments: Although this is a minor point, and this is not specifically pointing a finger at the author of this paper, I really don't like the term 'safeguard'. This term is now overutilized to add hype to papers, when 'is necessary' is sufficient. In this case, unless the answer is provided as to 'against what stil is safeguarding germ cells', this term is not meaningful. For example, if one can show that stil specifically senses germline-specific threat and tweaks the regular apoptotic pathway based on germline-specific needs, then the term 'safeguard' may be warranted.

Response:

In light of the reviewer's comment, we have revised the title of the manuscript to replace 'safeguard' with 'ensure,' which better reflects the demonstrated function of Stil without overstating its role. The new title of the manuscript is: 'Transcriptional Repression of reaper by Stand Still Ensures Female Germline Development in Drosophila'

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

In this well-executed study, Matsui et al. investigate how the female Drosophila germline prevents inappropriate apoptosis during development. They identify stand still (stil) as a key germline-specific repressor of apoptosis. Stil mutant flies are homozygous viable but female sterile due to widespread germ cell loss at the time of eclosion, which is driven by activation of the pro-apoptotic gene reaper (rpr) and caspase-dependent cell death. Germline-specific expression of anti-apoptotic factors such as p35 can rescue this phenotype, confirming that the defect lies in apoptotic regulation. The authors show that Stil directly represses rpr transcription through its BED-type zinc finger domain. Notably, undifferentiated germline cells remain resistant to apoptosis in the absence of stil, which the authors attribute to a silenced chromatin state at the rpr locus, marked by H3K9me3. These findings support a dual mechanism of protection: transcriptional repression of rpr by Stil, and a potential parallel chromatin-based silencing mechanism operating specifically in undifferentiated cells.

Major Issues:

1. Clarify cell identity in Figure 2E: It is unclear whether the apoptotic cells shown are somatic or germline in origin. Including a somatic marker such as 1B1 would allow the reader to clearly distinguish the apoptotic population and better interpret the figure.

Response:

We thank the reviewer for this helpful suggestion. Occasionally, the signal of the germline marker Vasa can be attenuated in dying germline cells. As suggested by the reviewer, we also tested α-Spectrin (a plasma membrane and fusome marker) instead of 1B1 together with TUNEL labeling, but this approach did not clearly distinguish somatic from germline apoptotic cells. To directly clarify cell identity, we now provide an improved co-stained image in which TUNEL-positive nuclei are surrounded by Vasa-positive cytoplasm, indicating a germline origin. Figure 2E has been updated accordingly.

New Fig. 2E;

Quantification of undifferentiated cells in mutants: There appears to be inconsistency in the representation of undifferentiated germ cells across figures. Early panels show near-complete germline loss, while later analyses focus on undifferentiated cells that are reportedly apoptosis-resistant. The authors should quantify the proportion of ovarioles retaining undifferentiated cells and present this data in Figure 1 or the supplements to resolve this discrepancy.

Response:

Thank you for raising the important point regarding the apparent inconsistency in the representation of undifferentiated germ cell populations. In early panes (Fig.1C, D), we analyzed adult ovaries of stil loss-of function mutants where all germline cells including undifferentiated germline stem cells (GSCs) are almost completely lost (Fig. 1C), showing nearly 100% agametic ovarioles. However, in later analysis such as those in Fig. 5A, B, we showed 3rd instar-larval ovaries of stil loss-of function mutants containing a few surviving germline cells nearby the future cap cell, the niche providing stem cell ligand, Decapentaplegic (Dpp) (Xie & Spradling, 1998). This suggests that Dpp-responsive undifferentiated germline cells may be relatively resistant to apoptosis caused by stil loss.

Indeed, the GSC-like cells generated by the overexpression of a constitutively active form of Dpp receptor, Thickveins (Tkv.CA) or loss of the differentiation factor bam, were resistant to apoptosis caused by stil loss (Fig. 5C, D). These GSC-like cells may possess enhanced stemness, owing to either excessively elevated Dpp signaling or complete loss of bam, which could lead to stronger repression of rpr expression through tighter chromatin compaction.

We added this argument in the Results section of the revised manuscript as follows.

Revised Page 16, Line 361; Compared to GSCs, which were almost completely lost in stil mutants, GSC-like cells may retain a more robust stemness owing to the extremely elevated Dpp signaling pathway, potentially resulting in stronger repression of rpr expression.

Interpretation of chromatin state at the rpr locus: The claim that H3K9me3, but not H3K27me3, marks the rpr locus is not fully convincing given the low ChIP-seq signal shown. Including a comparison to a known positive control locus would strengthen the argument. Alternatively, the authors could broaden the discussion to include global chromatin reorganization during germ cell to maternal transition, as reported in Kotb et al., 2024 and how such changes may impact rpr accessibility. Also stl mutant rescued with P53 have a "string of pearls" phenotype that are associated with germ cell to maternal transition defects (Figure S3, p53 OE)

Response:

We thank the reviewer for the thoughtful and constructive comment regarding the interpretation of chromatin state at the rpr locus. To strengthen the inference that the rpr locus shows H3K9me3 enrichment, whereas clear H3K27me3 enrichment is not evident, we have now included ChIP-seq signal profiles for known positive control loci, using light (lt) as an H3K9me3-enriched locus (Akkouche et al., 2017; Greil et al., 2003) and Ultrabithorax (Ubx) as a canonical H3K27me3 target (Torres-Campana et al., 2022). These comparisons support our interpretation that H3K9me3, rather than H3K27me3, characterize chromatin around the rpr locus in GSCs. Accordingly, while we do not exclude a minor H3K27me3 contribution, our analyses indicate H3K9me3 as the predominant signature at rpr in GSCs.

New Fig.6B and 6C;

The legend of new Fig. 6B and Fig. 6C;

(B) H3K9me3 ChIP-seq signal at the rpr locus and the lt locus (H3K9me3-positive control) in GSCs and 4C NCs. (C) H3K27me3 ChIP-seq signal at the rpr locus and the Ubx locus (H3K27me3-positive control) in GSCs and 32C NCs.

A sentence of Result section was revised as below.

Revised Page 17, Line 396; As internal controls, we confirmed H3K9me3 enrichment at the light (lt) locus and H3K27me3 enrichment at the Ultrabithorax (Ubx) locus, consistent with their established chromatin states (Akkouche et al., 2017; Greil et al., 2003; Torres-Campana et al., 2022); relative to these controls, the rpr locus shows H3K9me3 but no clear H3K27me3 enrichment in GSCs.

Regarding the suggestion to broaden the discussion to include global chromatin reorganization during the germline-to-maternal transition, as reported in Kotb et al., 2024, we agree that this is an important avenue for understanding rpr accessibility. The "string of pearls" phenotype observed in stil mutants rescued with P35 overexpression (Figure S3) is consistent with perturbations during this transition. However, a detailed analysis of such chromatin reorganization and its potential impact on rpr regulation lies beyond the scope of the present study and represents a valuable direction for future work.

Broader analysis of rpr regulation in somatic cells: It would be informative to examine publicly available chromatin or transcriptional data for the rpr locus in somatic ovarian cells. This could help clarify whether rpr regulation by Stil is truly germline-specific or reflects broader developmental trends. This will also clarify why the flies are homozygous viable but female sterile.

Response:

We thank the reviewer for this insightful suggestion. We agree that exploring chromatin accessibility and transcriptional regulation at the rpr locus in somatic ovarian cells would provide valuable insights into tissue- or cell-type-specific chromatin environments that influence rpr expression.

However, to our knowledge, there are currently no publicly available ATAC-seq or comparable chromatin datasets for purified ovarian somatic cells, including follicle cells or ovarian somatic cells (OSCs). As such, we are unable to incorporate this analysis in the current study. Nevertheless, we fully recognize the importance of this line of inquiry and consider it a valuable direction for future research.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary:

This manuscript describes the characterization of stand still (stil), a previously identified gene needed for germ cell survival in Drosophila. The molecular function of Stil has until now remained poorly understood. This new work shows that loss of stil results in reaper (rpr)-dependent apoptosis within female germ cells. Loss of rpr suppresses many of the phenotypes observed in stil mutants. Experiments performed using Drosophila cell culture suggest that Stil binds to elements within the rpr promoter. DamID and structure/function experiments indicate that Stil likely directly represses the transcription of rpr within germ cells.

In general, the experiments are well executed, and the data largely support the basic claims of the authors. Replicates are included and appropriate statistical analyses have been provided. The text and figures clear and accurate. Appropriate references were cited. There are a few things the authors should address or rephrase before publication.

On page 9 line 190-192. The authors state "Altogether, these findings indicate that the loss of stil function not only triggers apoptosis that can be suppressed by apoptosis inhibitors but also causes defects in oogenesis progression that are not rescued by blocking cell death." Failure to rescue defects during mid-oogenesis could be due to insufficient transgene expression. Indeed, loss of rpr appears to rescue the fertility of stil mutants. The conclusions of this section should be restated.

Response:

We agree that the failure to rescue mid-oogenesis defects by P35 overexpression may, at least in part, be due to insufficient transgene expression. This explanation is particularly plausible given that loss of rpr more effectively restored fertility in stil mutants. As suggested by the reviewer, we have revised the relevant sentences, to avoid misinterpretation as below.

Revised Page 9, Line 191; Altogether, these findings indicate that the loss of stil function triggers apoptosis that can be suppressed by apoptosis inhibitors.

Revised Page 12, Line 253; The complete rescue of germline survival in stil rpr double mutants also suggests that the failure of P35 overexpression to restore mid-oogenesis defects may partly reflect insufficient transgene expression (Fig. S3).

The authors should present the overlap between genes that change expression in a stil mutant and those in which the DamID experiments indicate are directly bound by Stil protein. DamID can sometimes give spurious results depending on expression levels. Further discussion along this point is necessary.

Response:

We thank the reviewer for raising this issue. As suggested, we have now analyzed the overlap between genes that are differentially expressed in stil mutant ovaries (identified by RNA-seq with stil mutant expressing P35) and genes that are potentially bound by Stil based on DamID-seq data (promoter-proximal peaks {less than or equal to}1 kb) as Supplementary Table 4. The list includes genes with DamID peaks within promoter regions and that also exhibit significant differential expression (|log2FC| > 1, adjusted p The overlap between DamID-seq and RNA-seq comprises 682 genes, including rpr, supporting the idea that Stil regulates rpr expression through interaction with its upstream promoter region. However, the detected peak signal at rpr was 3.41, which was not that strong, suggesting that Stil may also bind to and regulate other genes in female germline cells. Investigating the potential role of Stil in regulating other genes represents an important future direction of our study.

We have included this analysis and argument in the revised manuscript as below.

Revised Page 13, Line 280; A total of 682 genes with Stil-enriched peaks detected at promoter regions ({less than or equal to}1 kb) showed significantly altered expression in RNA-seq analysis of stil mutants expressing P35, including rpr (Supplementary Table 4).

Revised Page 20, Line 440; Notably, the DamID peak intensity at the rpr locus reached 3.41, which is moderate rather than strong (Supplementary Table 4). This suggests that, in addition to repressing rpr, Stil may bind to and regulate other genomic loci in the female germline. Investigating the repertoire of Stil target genes and elucidating their roles in germline cells will be an important future direction of this study.

For structure function experiments, a western blot showing expression levels of the different transgenes in ovaries should be included.

Response:

We thank the reviewer for this helpful comment. To address this point, we examined the expression levels of the four Stil variants (FL, NT, CT, and AAYA) in ovaries driven by a germline driver under a wild-type background using Western blotting. The representative blot and quantification from three biological replicates showed comparable expression levels among the variants, with the CT variant displaying a slightly reduced signal. Importantly, AAYA showed expression comparable to FL yet, like CT, failed to rescue, indicating that the rescue failure is not explained by expression-level differences. These data instead support a requirement for the BED-type zinc finger for Stil function in the germline. While we cannot fully exclude a minor contribution from the slightly lower expression of the CT variant to the lack of rescue, the AAYA result argues that loss of BED-type zinc-finger function is the primary cause; we note this caveat in the revised text. The corresponding data are now presented in Figure S6A of the revised manuscript.

New Fig. S6A;

The legend of new Fig. S6A;

(A) Western blot analysis of 6×Myc-tagged Stil variants (FL, NT, CT, and AAYA) driven by NGT40-Gal4; NosGal4-VP16, with y w as a control. Stil variants were detected with anti-Myc, and α-Tubulin (αTub) served as a loading control. Arrowheads indicate Stil variant proteins. The lower panel shows quantification of the Myc/αTub signal ratio normalized to FL. Error bars indicate standard deviation (s.d.) (n = 3).

A sentence of Result section was revised as below.

Revised Page 13, Line 291; The expression of all four Stil variant proteins from the transgenes was confirmed, although Stil-CT showed a slightly reduced expression level (Fig. S6A)

Revised Page 14, Line 305; Although CT shows slightly lower expression, AAYA fails to rescue despite FL-like expression, indicating that expression level is not limiting and that loss of the BED-type zinc finger underlies the phenotype.

"With the addition of the new Fig. S6A, the following figure labels have been updated;

Fig. S6A →S6B

Fig. S6B → S6C

Fig. S6C → S6D

Fig. S6D → S6E

Individual data points should be shown in each graph in place of simple bar graphs. This type of presentation was inconsistent throughout the paper.

Response:

We thank the reviewer for this constructive comment. In line with the reviewer's suggestion, we have revised the relevant graphs to include individual data points overlaid on bar plots with error bars. This modification enables readers to better assess data variability. We also ensured consistency in data presentation among the revised figures while maintaining clarity throughout the manuscript.

Reference "G & D., 1997" should be properly formatted.

Page 6 line 117 and 121- a couple of instances where "cell" should be "cells"

Page 14 line 304- typo "Still"

Response:

As suggested, we have revised all figures to display individual data points in each graph instead of using simple bar graphs. This change has been applied consistently throughout the manuscript to improve data transparency and readability. The revised figures include Figure 1A, 2B, S1A, and S2A.

We have also corrected the following textual issues;

・The reference "G & D., 1997" has been properly formatted as "Pennetta & Pauli, 1997".

・On page 6, lines 119 and 123, "cell" has been corrected to "cells" to ensure grammatical accuracy.

・On page 14, line 315, the typo "Still" has been corrected to "Stil".

Reviewer #3 (Significance (Required)):

The significance of the work lies in characterizing a previously unknown function of Stil. By showing that Stil acts to repress transcription of the cell death gene rpr, the authors provide new insights into how programmed cell death is regulated in the Drosophila female germline. Readers interested in reproductive biology, cell death, chromatin, and general developmental biology will find value in these new findings.

One thing to consider is the possibility that Stil represses rpr in the context of the double strand breaks that form during meiosis. Experiments in the paper indicate that stil knockdown results in TUNEL labeling in region 2A/2B of the germarium. The authors should consider co-labeling for a meiosis marker (C(3)G or gammaH2Av) to see if this PCD correlates with this expression. In addition, they could test whether loss of Spo11 (mei-W68) suppresses stil phenotypes during early germ cell development. Relating the function of Stil to repression of cell death during this critical time of germ cell development would elevate the impact and significance of the paper. However, this may be considered beyond the scope of the current study.

Response:

We deeply thank the reviewer for this insightful and thought-provoking suggestion.

As suggested, we conducted co-staining with γH2Av (DBS marker), as well as genetic interaction experiments with Spo11 (mei-W68) mutants to address this question shown below. In region 2 across all genotypes including y w control, and stil heterozygous and homozygous ovaries expressing P35, γH2Av signals were discernible and subsequently lost in region 3 through the meiotic recombination-specific DNA repair program (Additional Figure A). In stil mutants, however, an additional strong γH2Av signal was specifically observed in the oocyte, beyond the expected meiotic pattern. Furthermore, loss of meiotic recombination factors, including mei-W68, in stil mutants partially rescued the germline loss phenotype, although not to the same extent as in rpr mutants (Additional Figure B, C: 43.5 % in mei-W68-GLKD, 23.9 % in mei-P22P22 and 12.8 % in vilya826 versus 100 % with loss of rpr in Fig. 3E, F of the revised manuscript). These findings suggest that accumulation of meiotic DSBs is not the main cause of rpr upregulation in stil mutants. We feel that these analyses are beyond the scope of the current study, which focuses on identifying Stil as a transcriptional repressor of rpr and characterizing its role in germline apoptosis. Elucidating other mechanisms that elevate rpr expression in stil mutants will be the focus of future work. Hence, we are providing these data here for the reviewer's reference, but if the reviewer prefers, we would be happy to incorporate them into the manuscript.

Additional Figure (A) Immunostaining of ovarioles from y w, stilEY16156/CyO; P35 OE (NGT40; NosGal4-VP16> P35), stilEY16156; P35 OE flies with antibody against DNA double-strand break marker H2Av (green), Vasa (red), and DAPI (blue). Insets show enlarged views of egg chamber. White dots indicate oocyte nuclei, Scale bar: 50 μm (ovariole) and 20 μm (egg chamber). (B) Immunofluorescence of Vasa (red) and DAPI (blue) in ovaries from stilEY16156, stilEY16156; mei-W68-GLKD (driven by NGT40; NosGal4-VP16), stilEY16156; meiP22P22, and stilEY16156; vilya826. Scale bar: 50 μm. (C) Quantification of the percentage of ovarioles containing germline cells in 2-3-day-old females. The genotypes of females are indicated below the x-axis, and the number of germaria analyzed is shown above each bar. Error bars represent the standard deviation (s.d.).

Akkouche, A., Mugat, B., Barckmann, B., Varela-Chavez, C., Li, B., Raffel, R., Pélisson, A. & Chambeyron, S. (2017). Piwi Is Required during Drosophila Embryogenesis to License Dual-Strand piRNA Clusters for Transposon Repression in Adult Ovaries. Molecular Cell, 66(3), 411-419.e4. https://doi.org/10.1016/j.molcel.2017.03.017

Greil, F., Kraan, I. van der, Delrow, J., Smothers, J. F., Wit, E. de, Bussemaker, H. J., Driel, R. van, Henikoff, S. & Steensel, B. van. (2003). Distinct HP1 and Su(var)3-9 complexes bind to sets of developmentally coexpressed genes depending on chromosomal location. Genes & Development, 17(22), 2825-2838. https://doi.org/10.1101/gad.281503

Röper, K. & Brown, N. H. (2004). A Spectraplakin Is Enriched on the Fusome and Organizes Microtubules during Oocyte Specification in Drosophila. Current Biology, 14(2), 99-110. https://doi.org/10.1016/j.cub.2003.12.056

Torres-Campana, D., Horard, B., Denaud, S., Benoit, G., Loppin, B. & Orsi, G. A. (2022). Three classes of epigenomic regulators converge to hyperactivate the essential maternal gene deadhead within a heterochromatin mini-domain. PLoS Genetics, 18(1), e1009615. https://doi.org/10.1371/journal.pgen.1009615

Xie, T. & Spradling, A. C. (1998). decapentaplegic Is Essential for the Maintenance and Division of Germline Stem Cells in the Drosophila Ovary. Cell, 94(2), 251-260. https://doi.org/10.1016/s0092-8674(00)81424-5

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Reply to the reviewers

Point-by-Point Response to Reviewers for Manuscript #RC-2024-02720

Manuscript Title: Molecular and Neural Circuit Mechanisms Underlying Sexual Experience-dependent Long-Term Memory in Drosophila.

Corresponding Author: Woo Jae Kim

We extend our sincere gratitude to the Managing Editor and both reviewers for their diligent and insightful evaluation of our manuscript. The comprehensive feedback provided has been invaluable, guiding us to significantly strengthen the manuscript's scientific rigor, logical cohesion, and overall impact. We have undertaken a substantial revision, incorporating new experimental evidence, reframing the central narrative, and improving data presentation to address all concerns raised.

The major revisions include:

1. New Experimental Evidence: We have performed three new sets of experiments to address key questions raised by the reviewers. First, we used the protein synthesis inhibitor cycloheximide to pharmacologically validate that the observed memory is indeed a form of long-term memory (LTM). Then, we performed genetic intersectional analyses to determine if the identified Yuelao (YL) neurons express the canonical sex-determination transcription factors doublesex (dsx) and fruitless (fru).
2. Narrative Reframing and Logical Restructuring: We fully agree with the reviewers that the logic of the original manuscript was confusing, particularly regarding the distinction between the broad Mushroom Body (MB) Kenyon Cell (KC) population and the specific YL neurons. The manuscript has been extensively rewritten to present a clear, hypothesis-driven narrative. We now frame the initial KC-related findings as part of a broader screening effort that logically led to the identification and focused investigation of the YL neuron circuit.
3. Refined Central Claim: Guided by the reviewers' feedback and our new data, we have sharpened our central claim. We now propose that YL neurons constitute a critical circuit for forming attractive taste- and pheromone-based memories derived from Gr5a neuronal inputs. This form of appetitive memory is distinct from the previously characterized internal reward state associated with ejaculation, adding a new layer to our understanding of how male flies remember and evaluate reproductive experiences.
4. Improved Data Quality and Analysis: In response to valid critiques, all imaging figures have been replaced with high-resolution versions. Furthermore, our methods for fluorescence quantification, particularly for the TRIC calcium imaging experiments, have been corrected to include normalization against an internal reference channel, adhering to established best practices. All requested genetic control experiments have been performed. We are confident that these comprehensive revisions have fully addressed all concerns and have transformed our manuscript into a much stronger, more focused, and logically sound contribution. We thank you again for the opportunity to improve our work and look forward to your evaluation of the revised manuscript.

Responses to Reviewer #1

General Comments: This study explores the molecular and neural circuitry mechanisms underlying sexual experience-dependent long-term memory (SELTM) in male Drosophila. The authors use behavioral, imaging, and bioinformatics approaches to identify YL neurons, a subset of mushroom body (MB) projecting neurons, as crucial for SELTM formation. They propose that YL neurons receive inputs from WG neurons via the sNPF-sNPFR pathway and implicate molecular players such as orb2, fmr1, MDAR2-CaMK, and synaptic plasticity in their function.

However, the evidence presented does not adequately support the authors' claims. The data fail to cohesively tell a logical story, and key conclusions appear to be based on assumptions and correlations rather than robust evidence.

• Answer: We are deeply grateful to both reviewers for their thorough and constructive evaluation of our manuscript. Their collective feedback has been instrumental in helping us to clarify the study's rationale, strengthen our interpretations, and significantly improve the overall quality and impact of the work. We appreciate the recognition of our study's potential to advance the understanding of how sexual experience modifies future mating behaviors and to elucidate the neuronal and molecular mechanisms of how memory regulates a key sexual behavior in male Drosophila*.

• *In response to the general comments, we have undertaken a major revision of the manuscript to improve the clarity, logic, and presentation. We have rewritten the Abstract and Introduction to more clearly define "sexual experience-dependent long-term memory" (SELTM) and articulate its significance in the context of adaptive decision-making and interval timing. The entire manuscript has been restructured to present a more logical, hypothesis-driven narrative that clearly distinguishes our initial broad screening from the focused investigation of the YL neuron circuit. We have also incorporated alternative interpretations of our data, particularly regarding the role of the YL circuit in regulating baseline mating duration in naive males, which has added more depth to the study. Finally, all figures have been remade in high resolution, and all requested genetic controls and methodological clarifications have been added to ensure rigor and reproducibility. We are confident that these revisions have addressed the reviewers' concerns and have resulted in a much stronger manuscript.

Comment 1: The study identifies the knowledge gap (lines 103-104) but fails to integrate relevant literature, particularly Shohat-Ophir et al., Science (2012), and Zer-Krispil et al., Curr Biol (2018). These studies established that ejaculation induces appetitive memory in male Drosophila via corazonin and NPF neurons. The current study does not provide direct evidence that the "act of mating itself" drives SELTM, as it includes both courtship and copulation.

Response: Thank you for highlighting these two landmark studies. We fully agree that Shohat-Ophir et al., Science (2012) and Zer-Krispil et al., Curr Biol (2018) were pivotal in demonstrating that ejaculation—and the accompanying corazonin/NPF signalling—can establish an appetitive memory in males.

In the revised manuscript we have now integrated both papers on lines 111-118:

“Previous work has shown that successful copulation is intrinsically rewarding to male Drosophila: a single mating encounter elevates brain neuropeptide F (NPF) levels and suppresses subsequent ethanol preference19. Importantly, Zer-Krispil et al. further demonstrated that ejaculation itself—artificially induced by optogenetic activation of corazonin (Crz) neurons—is sufficient to mimic this reward state, driving appetitive memory formation and up-regulation of NPF. These findings indicate that the act of ejaculation, rather than the entire courtship sequence, is the critical sensory event that gates post-mating reward.”

Comment 2: The nature of the observed long-lasting reduced mating duration requires clearer characterization: Is this an associative memory or experience-dependent behavioral plasticity? Can the formation of this long-term memory be blocked by protein synthesis inhibitors, such as cycloheximide?

Response: We thank the reviewer for this excellent suggestion to pharmacologically characterize the nature of the memory. To definitively test whether the observed SMD is a form of protein synthesis-dependent long-term memory (LTM), we performed a new experiment as suggested.

We have now included data in new Figure supplement 1I showing that feeding males the protein synthesis inhibitor cycloheximide (CXM) for 24 hours immediately following the sexual experience completely blocks the formation of the long-lasting SMD phenotype. Control flies fed a vehicle solution exhibited robust SMD. This result provides strong evidence that SELTM is not merely a form of transient behavioral plasticity but is a genuine form of LTM that requires de novo protein synthesis for its consolidation, a hallmark of LTM across species.[1]

The revised text was put on lines 173-176:

" To determine whether the persistent reduction in mating duration (SMD) depends on de-novo protein synthesis, we fed males the translational inhibitor cycloheximide (CXM). Under this regimen, CXM completely abolished the SMD phenotype (Fig. 1I)."

Comment 3: While schematics illustrate the working hypotheses, the text lacks detailed explanations, leaving the reader unclear about the rationale behind certain conclusions.

__Response: __Thank you very much for this insightful comment. We fully agree that the original manuscript did not provide sufficient textual justification for the conclusions derived from the schematics. In the revised version we have therefore added comprehensive explanations immediately following each figure (or schematic) that explicitly state the underlying rationale, the key observations supporting our hypotheses, and the logical steps leading to each conclusion. We believe these additions now make the reasoning transparent and easy to follow. We appreciate your feedback, which has substantially improved the clarity of our work.

• *

Comment 4*: The logic to draw certain conclusions was confusing and misleading. - For instance, the role of orb2 in SELTM is examined via knockdown in MB Kenyon cells (KCs) (using ok107>orb2-RNAi), which is irrelevant to the claim that orb2 functions in YL neurons. Additionally, RNAseq analyses (Fig. 1N-S) focusing on orb2 expression in a/b KCs are irrelevant to and cannot support the claim that Orb2 functions in YL neurons. *

*- Similarly, the claim (lines 302-303) that sNPF-R expression is exclusive to MB KCs conflicts with data showing effects when sNPF-R is knocked down in YL neurons. How can knocking-down a gene, which is exclusively expressed in neural population A, in neural population B affect a phenotype? This inconsistency undermines the interpretation of the results. *

*- Other examples include lines 223-227 and lines 246-249. It is very confusing how the authors came to the indications. *

- The authors also kept confusing the readers and themselves by mistakenly referring to MB KC a-lobe and YL a-lobe projection. They may know the difference between the two neural populations but they did not always refer to the right one in the text.

Response: We agree completely with the reviewer that the logic in the original manuscript was confusing and failed to clearly distinguish between the general MB Kenyon Cell (KC) population and the specific YL projection neurons. This was a major flaw, and we are grateful for the opportunity to correct it. We have undertaken a major revision of the manuscript's narrative and structure to present a clear, logical progression of discovery.

The new logical flow of the manuscript is as follows:

1. We first establish that sexual experience induces a robust, long-lasting SMD behavior that is dependent on protein synthesis
2. We then perform initial experiments to implicate the MB as a key brain region. We show that broad inhibition of MB KCs (using the ok107-GAL4 driver) disrupts SMD behavior.This result establishes the general involvement of the MB but lacks cellular specificity.
3. The remainder of the manuscript then focuses specifically on dissecting the molecular and cellular properties of these YL neurons. Finally, we have meticulously edited the entire manuscript to ensure that we always use precise terminology, clearly distinguishing between "YL neuron projections to the MB α-lobe" and the "MB KC α-lobe."

Comment 5*: The imaging figures provided are unfocused and poorly resolved, making it difficult to assess data quality. *

*- Colocalization analyses of orb2 and YL are unconvincing... Maximum intensity projection images are insufficient... complete image stacks with staining of orb2, YL, and KCs (MB-dsRed) are needed for validation. *

- Quantification of imaging data appears flawed. For example, claims of orb2 and CaMKII upregulation in MB a-lobe projections (e.g., Fig. S2F-J, Fig. 3M,N) are confounded by widespread increases in intensity across the brain, lacking specificity.

• *

*- The TRIC experiment analysis should normalize GFP signals to internal reference channel (RFP in the TRIC construct)... *

- In Fig. 6H-J, methods for counting synapse numbers are not described. How are synapse numbers counted in these low-resolution images?

Response: We sincerely apologize for the poor quality of the imaging data presented in the original manuscript. We agree with the reviewer's critiques and have taken comprehensive steps to rectify these issues.

• Image Quality: We apologize for not including the full image data in the original submission. The complete figure is now presented in revised Fig. 2J .
• Fluorescence Quantification: The fluorescence quantification has been re-analyzed. The Methods section now includes a detailed description of our protocol.
• TRIC Normalization: We apologize for not stating this explicitly in the previous version. As now described in the revised Methods subsection “Quantitative Analysis of Fluorescence Intensity”, all TRIC images were acquired with identical laser power and exposure settings. The GFP signal was background-corrected and then normalized to the RFP fluorescence encoded by the TRIC construct itself (UAS-mCD8RFP), which serves as an internal reference for construct expression and mounting thickness.

• Synapse Counting: We agree with the reviewer that the resolution of our images was insufficient for accurate synapse particle counting. We have therefore removed the problematic analysis from the former Fig 6H-J. Our conclusions regarding synaptic plasticity now rest on the more robust and quantifiable data showing a significant increase in the total area of dendritic (DenMark) and presynaptic (syt.eGFP) markers. Comment 6: The study presents data from unrelated learning paradigms (e.g., olfactory associative learning, courtship conditioning; Fig. 7) without justifying how these paradigms relate to SELTM. Particularly, the authors claimed that SELTM is related to Gr5a, which leads to appetitive memories, which involve PAM dopaminergic neurons and MB horizontal lobes. However, the olfactory associative learning with electric shock and courtship conditioning lead to aversive memories, that involve PPL1 dopaminergic neurons and the vertical lobes.

• *

Response: We thank the reviewer for requesting clarification on the rationale for including these experiments. The purpose of these assays was to test the specificity of the YL neuron circuit. A key question is whether YL neurons represent a general-purpose LTM circuit or one specialized for a particular memory modality.

The data show that knockdown of Orb2 or Nmdar2 specifically in YL neurons has no effect on the formation of LTM for aversive olfactory conditioning or aversive courtship conditioning. These negative results are critically important, as they demonstrate that the YL circuit is

not required for all forms of LTM. This finding strongly supports our revised central claim that YL neurons are specialized for processing appetitive memories derived from the specific sensory context of mating (i.e., taste and pheromonal cues from Gr5a neurons).

To improve the narrative flow of the main text, We rearranged the order of the articles. The relevant description is in lines 398-401:

“To determine whether YL neurons constitute a general LTM circuit or are dedicated to the appetitive context of mating, we tested two canonical aversive paradigms: electric-shock olfactory conditioning and courtship conditioning. If YL neurons serve as a universal LTM module, their genetic impairment should also impair aversive memory.”

lines 469-472:

“The inability of YL perturbation to impair aversive memories (Fig. 7) corroborates that this micro-circuit is dedicated to Gr5a-dependent SELTM rather than acting as a generic LTM hub”

Minor Issues

Comment 1: Fig 2F. YL projections are labeled as MBONs. Clarify whether YL neurons are the upstream or downstream (MBON) of KCs.

__Response: __Thank you for this helpful comment. As Huang et al., 2018[2] (Nat. Commun. 9:872) have mentioned, the MB093C-GAL4 driver is the MBON-α3 mushroom body output neuro. Consequently, YL neurons are positioned downstream of the MBON-α3.

We have now clarified this point in the revised manuscript lines 217-222:

“Each of these neurons extends a vertical fiber to the dorsal brain region, where they form dense arbors within the α-lobes of the mushroom body. Because the MB093C-GAL4 driver labels MBON-α3 output neuron[51], these YL arbors are positioned postsynaptically within the α-lobe and relay mushroom-body output to the anterior, middle, and posterior superior-medial protocerebrum.”

Comment 2: Extensive language polishing is required, as several sentences are unclear (e.g., lines 169-172).

Response: We apologize for the lack of clarity in the original text. The entire manuscript has undergone extensive revision and professional language editing to improve readability, precision, and grammatical accuracy.

Responses to Reviewer #2

Major Comments

Comment 1: Clearer articulation of the rationale, motivation, and significance of the overall study design and individual experiments can strengthen the manuscript and promote readership. For example, the beginnings of the abstract and introduction should define what authors mean by sexual experience-dependent long-term memory and its significance (including why it is "significant for reproductive success" (lines 46 and 92)). Similarly, employing more concrete language throughout the text will help anchor and contextualize the study. Interpretation is occasionally insufficient or does not follow directly from the data provided.

Response: We thank the reviewer for this valuable advice. We agree that the motivation and significance of our study were not articulated clearly enough. We have rewritten the Abstract and the beginning of the Introduction to address this. The revised text now explicitly defines SELTM as a protein synthesis-dependent, appetitive memory formed in response to gustatory and pheromonal cues. We explain its significance in the context of adaptive behavior, linking it to interval timing, a process by which male flies strategically adjust their mating investment (i.e., mating duration) based on prior experience to optimize reproductive success and energy expenditure. This framing provides a clearer context for our investigation into its underlying neural and molecular mechanisms.

Comment 2: Long term memory: I do not work on Drosophila memory, but a cursory search suggests that the field generally considers long term memory in Drosophila to last for 24 hr to days (courtship memory lasts for >24 hr). SMD decays between 12-24 hr after copulation. Could SMD be considered a short-term effect?

Response: This is an important point of clarification, as described in our response to Reviewer #1 (Major Comment 2), we have performed a new experiment demonstrating that the formation of SMD is blocked by the protein synthesis inhibitor cycloheximide (Figure 1I). This dependence on de novo protein synthesis is a defining characteristic of LTM, distinguishing it from short- and intermediate-term memory forms.[1] where memories lasting 12-24 hours are well-established as forms of LTM.[3] Therefore, based on both its duration and its molecular requirements, SMD represents a bona fide form of LTM.

The relevant statement is in lines 174-178:

"To determine whether the persistent reduction in mating duration (SMD) depends on de-novo protein synthesis, we fed males the translational inhibitor cycloheximide (CXM). Under this regimen, CXM completely abolished the SMD phenotype (Fig. 1I). This finding suggests that the reduction in mating investment is contingent upon the formation of LTM."

Comment 3: Fig 1B-E share the same control (naive) group. If these experiments were performed in the same replicate(s), they should be plotted in the same figure. If not, please provide more details on how experimental blocks were set up and how controls compared between replicates.

Response: Thank you for this helpful suggestion. We understand that sharing the same naive control across multiple panels (Fig. 1B–E) may raise concerns about data independence. However, we chose to present these panels separately for the following reasons:

1. Clarity and Readability: Each panel (B–E) represents a distinct temporal condition (0 h, 6 h, 12 h, 24 h post-isolation). Separating them avoids visual clutter and allows readers to focus on one time point at a time, improving interpretability.

__ Consistency with Internal Controls:__

Although the naive group is identical across panels, each experimental block (i.e., each isolation time point) was run independently on same days, with internal controls (naive vs. experienced) included in every block. This ensures that statistical comparisons remain valid within each panel, even if the naive data overlap.

We have now added a clear statement in the figure legend explaining that the naive group is shared across panels and that each time point was tested independently with internal controls. This maintains transparency while preserving the visual clarity of the current layout.

Comment 4: Serial mating (Fig 1F-H): please provide details on the methods. How much time elapsed between successive matings? Is a paired statistical test used? Sperm depletion also affects mating duration, and without this information the authors' conclusion (lines 155-156) does not automatically follow from the data.

Response:

1. __ Interval between successive matings__ We have rewritten the Methods to state explicitly that “as soon as one copulation ended the male was transferred immediately to a fresh virgin female, so the next mating began immediately.”

we add new method:

" Serial mating ____duration ____assay

Serial mating duration assay was identical to the standard procedure except that each male was presented with four DF virgin females in immediate succession: upon termination of the first copulation the male was immediately put into a fresh chamber containing the next virgin, the timer was restarted at first contact, and this step was repeated until four complete matings were recorded or 5 min elapsed without initiation, whichever came first."

__ Statistical test__

We apologize for omitting this detail. Unpaired t-test was used: for male the mating duration before (naïve) and after sexual experience was recorded, yielding paired observations. Prism’s unpaired t-test module was therefore applied to evaluate the mean difference.

The figure legend now states “with error bars representing SEM. Asterisks represent significant differences, as revealed by the Unpaired t test and ns represents non-significant difference (**p __ Mating duration versus sperm depletion__

We apologize for not having made it clear that these two observations are complementary, not contradictory. Previous work has shown that when male Drosophila copulate repeatedly, mating duration remains stable even though the number of sperm transferred—and thus the number of progeny sired—declines progressively [4]

The revised text is as follows (lines235-241):

"Previous work has shown that when male Drosophila copulate repeatedly, mating duration remains stable even though the number of sperm transferred—and thus the number of progeny sired—declines progressively. This dissociation confirms that the constant mating duration we observe in our serial-mating experiment (Fig. 1F–H) is consistent with normal sperm depletion and does not compromise the conclusion that the experience-dependent reduction in mating duration reflects long-term memory."

Thank you for helping us improve the clarity of our study.

Comment 5: Mating duration assay: Which isolation interval was chosen for the rest of the SMD experiments? The 12 hr en masse mating setup is relatively uncommon among studies on courtship/copulation/post-copulatory phenotypes, and introduces uncertainty and variability in the number and timing of matings that occurred during the 12 hr-window. This source of variability and its implication in interpreting the data should be acknowledged. Moreover, the 3 studies referenced in the methods all house males in groups of 4, whereas this study uses groups of 40. Could density confound the manifestation of SMD?

Response: We thank the reviewer for these important methodological questions.

• Isolation Interval: We have clarified in the Methods that virgin females were introduced into vials for last 1 day before assay.
• Housing Density: This is an excellent point. To control for any potential effects of housing density itself, we have clarified that our "naive" control males are also housed in groups of 40 for the same duration as the "experienced" males. Therefore, the only difference between the two groups is the presence of females, isolating the effect of sexual experience from the effect of social density. Comment 6: SMD behavior: comparing orb2 mutants and controls (Fig 1M and Fig S1K-L), loss of orb2 actually reduces the mating duration in native males (mean ~15 min) relative to controls (~20 min), and have possibly no effect on experienced males (~15 min). This is inconsistent with the SMD behavior demonstrated in Fig 1B-E. The same pattern is found for mushroom body silencing (Fig 1P, Fig S1M-N), orb2 knockdown in YL neurons (Fig 2D, Fig S2A-B), Fmr1 knockdown in YL neurons (Fig 3D, Fig S2B, S3D) and most other experiments where mating duration is not significantly different between naive and experienced males. This might demonstrate a separate role of YL neurons and its related circuit in regulating mating duration in naive males. Could the authors discuss this interpretation? As an aside, plotting genetic controls next to experimental groups is customary and facilitates comparisons between relevant groups.

Response: Thank you very much for this insightful observation.

1. Baseline differences among genotypes We agree that absolute mating duration differs slightly between genotypes (e.g. naive orb2∆/+ about 15 min vs. wild-type CS about 20 min). Such differences are common when mutations or transgenes are introduced into distinct genetic backgrounds, and they do not affect the within-genotype comparison that is the essence of SMD (sexual-experience-dependent shortening of mating duration). Therefore, for every experiment we compared naive vs. experienced males of the identical genotype, keeping all other variables constant.

Consistency of SMD across figures

In every manipulation that disrupts SMD memory (orb2∆, MB silencing, orb2-RNAi in YL neurons, Fmr1-RNAi in YL neurons, etc.) the naive–experienced difference disappears, whereas the genetic controls retain a significant ΔMD. This is fully consistent with Fig. 1B–E and demonstrates that the memory trace, not the basal duration, is abolished.

Figure layout

Following your suggestion, we have re-ordered all bar graphs so that the relevant genetic controls are placed immediately adjacent to the experimental groups, making within-panel comparisons easier.

We hope these clarifications and adjustments address your concerns.

Comment 7: Bitmap figures: unfortunately the bitmap figures are compressed and their resolution makes it difficult to evaluate the visual evidence.

Response: We apologize for the poor quality of the figures. All figures in the revised manuscript, including the scRNA-seq plots, have been remade as high-resolution vector graphics to ensure clarity and detail. For better understanding, different colored illustrations are also placed next to the scRNA-seq.

Comment 8: Sexual dimorphism of YL neurons: many neurons involved in sexual behaviors express dsx and/or fru. Do YL neurons express them?

Response: This is an excellent question. To address it, we performed a new set of experiments using genetic intersectional tools to test for the expression of doublesex (dsx) and fruitless (fru) in YL neurons. Our analysis, presented in figure supplement 2B, reveals that YL neurons are indeed fru-negative and dsx-negative. We therefore conclude that YL neurons do not belong to the canonical fru- or dsx-expressing neuronal classes and are unlikely to be intrinsically sex-specific.

We add explanation in lines 223-229:

"Our further analysis confirmed the presence of only three pairs of nuclei near the SOG in male brains, whereas female brains exhibit a greater number of nuclei near the AL (Fig. 2I), suggesting subtle sexual dimorphisms in GAL4MB093C-expressing neurons. Importantly, these neurons do not overlap with either fru- or dsx-expressing cells: co-immunostaining for GFP and Fru or Dsx revealed almost no colocalization in any brain region examined (Fig. S2B), indicating that YL neurons are distinct from the canonical sex-specific fru/dsx circuits."

Comment 9: Genetic controls for some crucial experiments are not provided, e.g. Fig 2J, Fig S3C, Fig S3E-F Fig 5B-C, F, Q-R, Fig S5A-E.

Response: We thank the reviewer for their careful attention to detail. We have now performed all the missing genetic control experiments.

Comment 10: Colocalization experiments: please provide more detail on how fluorescence is normalized for each channel across images, especially when the overall expression of an effector is up- or down-regulated after mating.

Response: We have updated the Methods section under "Quantitative Analysis of Fluorescence Intensity" and "Colocalization Analysis" to provide a detailed description of our normalization procedure.

Comment 11: Please resolve this apparent contradiction on the expression of Nmdar1 and 2 in YL neurons. On line 261: "both receptors co-expressing in Orb2-positive MB Kenyon cells"; on line 279-281 "Nmdar1 is not expressed with YL neurons [...] whereas Nmdar2 is expressed in a single pair of YL neurons..."

Response: We apologize for this contradiction, which arose from the confusing narrative structure of the original manuscript. As detailed in our response to Reviewer #1 (Major Comment 4), we have reframed the manuscript.

Comment 12: Particle analysis (Fig 6H-J): experienced males seem to have more synapses but trend towards smaller average size. It would be helpful to show number of synapses and average size as paired data, or show that the total particle area is larger in experienced males.

Response: We agree with the reviewer that this analysis was inconclusive and potentially misleading due to the limitations of image resolution. As noted in our response to Reviewer #1, we have removed this particle analysis (former Fig 6H-J) from the revised manuscript. Our claim for increased synaptic plasticity is now supported by the more robust measurement of the total fluorescence area of the pre- and postsynaptic markers, which shows a significant increase in experienced males.

Minor Comments

We thank the reviewer for their meticulous attention to detail. We have addressed all minor comments as follows:

Comment 1: 1. Some figures (e.g. Fig 3M-R) and experiments (e.g. oenocyte scRNA-seq) are not referenced in the text. dnc data is shown alongside amn and rut but the rationale for its inclusion is not provided.

__Response: __Original Fig. 3M-R (now Fig,3 M-O) was referenced on line 283. The rationale for including dnc data (as a canonical memory mutant) is now clarified in the text on lines 187-189:

"To ask whether the same molecular machinery underlies the SMD that follows sexual experience, we tested three classical memory mutants: dunce (dnc), amnesiac (amn), and rutabaga(rut)."

Comment 2: Some references might not point to the intended article (e.g. ref 123).

__Response: __The reference list has been checked and corrected.

Comment 3. Please plot genetic controls next to experimental genotypes as they are a crucial part of the experiment.

__Response: __All relevant figures now include plots of genetic controls next to experimental genotypes.

Comment 4. The "estimation statistics" plots are not necessary since the authors show individual data points. To further enhance data transparency, the authors may consider reducing the alpha and/or dot size so the individual data points are more readily visible.

Response: Thank you for this helpful suggestion! We fully agree that data transparency is essential. After carefully testing lower alpha values and smaller dot sizes, we found that either change markedly obscured the dense regions of the distributions. So we didn't change the size of the point.

The estimation-statistics overlays are kept for two courteous reasons: (i) they provide an immediate visual estimate of the mean difference and its 95 % confidence interval, which is the key statistic we base our conclusions on, and (ii) they spare readers from having to cross-reference separate tables.

Comment 5. For accessibility, please avoid using green and red in the same plot.

__Response: __We fully agree that red–green combinations can be problematic for colour-vision-impaired readers. In the present manuscript, however, the only panel that juxtaposes pure red and pure green is the Fly-SCOPE co-expression data. These scRNA-seq plots are provided only as supportive reference; the actual quantitative conclusions are based on independent genetic and imaging experiments that use magenta, cyan, yellow, and greyscale palettes. Moreover, the scope images are accompanied by detailed text descriptions of the overlapping cell clusters, so no essential information is lost even if the colours are indistinguishable

Comment 6. Fly Cell Atlas: please show color scales used for each gene as the color thresholds are gene-specific by default.The 3-color overlap on SCope also makes it very difficult to see the expression pattern for each gene. One possibility is outlining the Kenyon cells on the tSNE plots and showing the expression for each gene of interest.

Response: Thank you for this helpful suggestion. To avoid the ambiguity that arises from RGB blending in the three-colour overlay, we have added a small colour-mixing diagram next to the t-SNE plots (revised Fig. 1). This key shows the exact hues produced by pairwise and three-way overlaps:

• Red + Green = Yellow

• Red + Blue = Magenta

• Green + Blue = Cyan

• Red + Green + Blue = White

Thus, yellow, magenta or cyan dots indicate co-expression of two genes, while white dots mark cells where all three genes are detected. this diagram allows readers to interpret overlap colours at a glance without re-entering SCope.

Comment 7. Please also refer to Fly Cell Atlas as such. SCope is a visualization platform that houses multiple datasets.

__Response: __The reference to Fly Cell Atlas was added.

Comment 8. Please introduce acronyms and genetic reagents the first time they are mentioned.

__Response: __All acronyms and genetic reagents are now defined upon their first use.

Comment 9. Line 184: please specify "split-GAL4 reagents" instead of "advanced genetic tools".

__Response: __We have replaced "advanced genetic tools" with the more specific term "Split-GAL4 reagents."

Comment 10. Line 187: there are a few other lines with p>0.05 or p>0.01, so "uniquely" is inaccurate. Are the p-values in Table 1 corrected for multiple testing?

__Response: __The term "uniquely" has been revised for accuracy. No correction for multiple testing was applied because each entry in Table 1 represents a single pairwise comparison (naive vs. exp). Thus only one p-value was generated per experiment.

Comment 11. Some immunofluorescence panels lack scale bars.

__Response: __Scale bars have been added to all immunofluorescence panels.

Comment 12. Fig S2G-I: do authors mean "naive" instead of "group"?

__Response: __The term "group" in Fig S2G-I has been corrected to "naive."

Comment 13. Movie 1 should be referenced when YL neurons are first introduced.

__Response: __Movie 1 is now referenced when YL neurons are first introduced in the text.

Comment 14. Is Fig 4L similar to Fig 6L-N?

__Response: __This error has been corrected after the article was reformatted

Comment 15. Fig 7: please plot olfactory conditioning experiment results as either percentages, preference index, or paired numbers. "Number of flies/tube" is not as informative.

__Response: __Thank you for pointing this out. The bars in Fig. 7 indeed represent paired numbers, but we realise this was not stated explicitly. We apologize for the lack of clarity. In the revised manuscript we explained it in detail in figure legend and method. In the figure, we also marked the percentage of flies that chose to avoid the side of the stimulus with gas, and explained it in the Figure legend.

Reference

1. Lagasse F, Devaud J-M, Mery F. A Switch from Cycloheximide-Resistant Consolidated Memory to Cycloheximide-Sensitive Reconsolidation and Extinction in Drosophila. J Neurosci. 2009;29: 2225–2230. doi:10.1523/jneurosci.3789-08.2009
2. Huang C, Maxey JR, Sinha S, Savall J, Gong Y, Schnitzer MJ. Long-term optical brain imaging in live adult fruit flies. Nat Commun. 2018;9: 872. doi:10.1038/s41467-018-02873-1
3. Tonoki A, Davis RL. Aging Impairs Protein-Synthesis-Dependent Long-Term Memory in Drosophila. J Neurosci. 2015;35: 1173–1180. doi:10.1523/jneurosci.0978-14.2015
4. Macartney EL, Zeender V, Meena A, Nardo AND, Bonduriansky R, Lüpold S. Sperm depletion in relation to developmental nutrition and genotype in Drosophila melanogaster. Evol Int J Org Evol. 2021;75: 2830–2841. doi:10.1111/evo.14373

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Referee #2

Evidence, reproducibility and clarity

Summary:

Sun et al. show that Orb2-expressing, glutamatergic mushroom body neurons (YL neurons) are central to the "shorter mating duration (SMD)" behavior, where males reduce their mating duration up to 12 hours after the initial copulation. The authors use SMD as a model for understanding sexual experience-dependent long-term memory in males. A few genes implicated in long-term memory (Fmr1, CrebB) are required in YL neurons for SMD. The Nmdar-CaMKII signaling pathways is also implicated, and mating attenuates Ca2+ signaling and increases synaptic plasticity in the mushroom body and subesophageal ganglion.

Major comments:

1. Clearer articulation of the rationale, motivation, and significance of the overall study design and individual experiments can strengthen the manuscript and promote readership. For example, the beginnings of the abstract and introduction should define what authors mean by sexual experience-dependent long-term memory and its significance (including why it is "significant for reproductive success" (lines 46 and 92)). Similarly, employing more concrete language throughout the text will help anchor and contextualize the study. Interpretation is occasionally insufficient or does not follow directly from the data provided.
2. Long term memory: I do not work on Drosophila memory, but a cursory search suggests that the field generally considers long term memory in Drosophila to last for 24 hr to days (courtship memory lasts for >24 hr). SMD decays between 12-24 hr after copulation. Could SMD be considered a short-term effect?
3. Fig 1B-E share the same control (naive) group. If these experiments were performed in the same replicate(s), they should be plotted in the same figure. If not, please provide more details on how experimental blocks were set up and how controls compared between replicates.
4. Serial mating (Fig 1F-H): please provide details on the methods. How much time elapsed between successive matings? Is a paired statistical test used? Sperm depletion also affects mating duration, and without this information the authors' conclusion (lines 155-156) does not automatically follow from the data.
5. Mating duration assay: Which isolation interval was chosen for the rest of the SMD experiments? The 12 hr en masse mating setup is relatively uncommon among studies on courtship/copulation/post-copulatory phenotypes, and introduces uncertainty and variability in the number and timing of matings that occurred during the 12 hr-window. This source of variability and its implication in interpreting the data should be acknowledged. Moreover, the 3 studies referenced in the methods all house males in groups of 4, whereas this study uses groups of 40. Could density confound the manifestation of SMD?
6. SMD behavior: comparing orb2 mutants and controls (Fig 1M and Fig S1K-L), loss of orb2 actually reduces the mating duration in native males (mean ~15 min) relative to controls (~20 min), and have possibly no effect on experienced males (~15 min). This is inconsistent with the SMD behavior demonstrated in Fig 1B-E. The same pattern is found for mushroom body silencing (Fig 1P, Fig S1M-N), orb2 knockdown in YL neurons (Fig 2D, Fig S2A-B), Fmr1 knockdown in YL neurons (Fig 3D, Fig S2B, S3D) and most other experiments where mating duration is not significantly different between naive and experienced males. This might demonstrate a separate role of YL neurons and its related circuit in regulating mating duration in naive males. Could the authors discuss this interpretation? As an aside, plotting genetic controls next to experimental groups is customary and facilitates comparisons between relevant groups.
7. Bitmap figures: unfortunately the bitmap figures are compressed and their resolution makes it difficult to evaluate the visual evidence.
8. Sexual dimorphism of YL neurons: many neurons involved in sexual behaviors express dsx and/or fru. Do YL neurons express them? If they do, they might be a subset of characterized and named dsx/fru neurons.
9. Genetic controls for some crucial experiments are not provided, e.g. Fig 2J, Fig S3C, Fig S3E-F Fig 5B-C, F, Q-R, Fig S5A-E.
10. Colocalization experiments: please provide more detail on how fluorescence is normalized for each channel across images, especially when the overall expression of an effector is up- or down-regulated after mating.
11. Please resolve this apparent contradiction on the expression of Nmdar1 and 2 in YL neurons. On line 261: "both receptors co-expressing in Orb2-positive MB Kenyon cells"; on line 279-281 "Nmdar1 is not expressed with YL neurons [...] whereas Nmdar2 is expressed in a single pair of YL neurons in both male and female brains".
12. Particle analysis (Fig 6H-J): experienced males seem to have more synapses but trend towards smaller average size. It would be helpful to show number of synapses and average size as paired data, or show that the total particle area is larger in experienced males.

Minor comments:

1. Some figures (e.g. Fig 3M-R) and experiments (e.g. oenocyte scRNA-seq) are not referenced in the text. dnc data is shown alongside amn and rut but the rationale for its inclusion is not provided.
2. Some references might not point to the intended article (e.g. ref 123).
3. Please plot genetic controls next to experimental genotypes as they are a crucial part of the experiment.
4. The "estimation statistics" plots are not necessary since the authors show individual data points. To further enhance data transparency, the authors may consider reducing the alpha and/or dot size so the individual data points are more readily visible.
5. For accessibility, please avoid using green and red in the same plot.
6. Fly Cell Atlas: please show color scales used for each gene as the color thresholds are gene-specific by default.The 3-color overlap on SCope also makes it very difficult to see the expression pattern for each gene. One possibility is outlining the Kenyon cells on the tSNE plots and showing the expression for each gene of interest.
7. Please also refer to Fly Cell Atlas as such. SCope is a visualization platform that houses multiple datasets.
8. Please introduce acronyms and genetic reagents the first time they are mentioned.
9. Line 184: please specify "split-GAL4 reagents" instead of "advanced genetic tools".
10. Line 187: there are a few other lines with p>0.05 or p>0.01, so "uniquely" is inaccurate. Are the p-values in Table 1 corrected for multiple testing?
11. Some immunofluorescence panels lack scale bars.
12. Fig S2G-I: do authors mean "naive" instead of "group"?
13. Movie 1 should be referenced when YL neurons are first introduced.
14. Is Fig 4L similar to Fig 6L-N?
15. Fig 7: please plot olfactory conditioning experiment results as either percentages, preference index, or paired numbers. "Number of flies/tube" is not as informative.

Significance

The manuscript describes an extensive and comprehensive set of experiments aimed at elucidating the role of a subset of mushroom body neurons in mediating a male post-mating sexual behavior, which the authors use as a model for sexual experience-dependent long-term memory. Long-term post-mating responses in females have been well characterized in Drosophila and other insects, but post-mating long term memory in males are less well understood despite a few studies reporting their importance in mating success. How males adjust their mating duration based on internal and external cues can reveal insights about decision making and interval timer mechanisms. This study represents a functional advancement in the neuronal and molecular mechanisms of how memory and experience regulates a sexual behavior in male Drosophila. Overall, the manuscript can significantly benefit from general editing on clearer articulation of rationale and more appropriate interpretations of data. Higher resolution versions of bitmap figures is also crucial. The SMD experiments invite an alternative interpretation of data that centers on YL neurons' role on regulating mating duration in naive males, which alongside other roles of the mushroom body demonstrated in this manuscript, could add more depth to the study.

The findings in this manuscript will be of interest to a specialized audience interested in memory, neural circuits of behavior, and Drosophila sexual behavior. I work on Drosophila sexual behavior and circuits, but lacking experience on memory research, I am not as familiar with the mushroom body and conditioning experiments.

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Referee #1

Evidence, reproducibility and clarity

This study explores the molecular and neural circuitry mechanisms underlying sexual experience-dependent long-term memory (SELTM) in male Drosophila. The authors use behavioral, imaging, and bioinformatics approaches to identify YL neurons, a subset of mushroom body (MB) projecting neurons, as crucial for SELTM formation. They propose that YL neurons receive inputs from WG neurons via the sNPF-sNPFR pathway and implicate molecular players such as orb2, fmr1, MDAR2-CaMK, and synaptic plasticity in their function.

However, the evidence presented does not adequately support the authors' claims. The data fail to cohesively tell a logical story, and key conclusions appear to be based on assumptions and correlations rather than robust evidence.

Major comments:

1. The study identifies the knowledge gap (lines 103-104) but fails to integrate relevant literature, particularly Shohat-Ophir et al., Science (2012), and Zer-Krispil et al., Curr Biol (2018). These studies established that ejaculation induces appetitive memory in male Drosophila via corazonin and NPF neurons. The current study does not provide direct evidence that the "act of mating itself" drives SELTM, as it includes both courtship and copulation.
2. The nature of the observed long-lasting reduced mating duration requires clearer characterization: Is this an associative memory or experience-dependent behavioral plasticity? Can the formation of this long-term memory be blocked by protein synthesis inhibitors, such as cycloheximide?
3. While schematics illustrate the working hypotheses, the text lacks detailed explanations, leaving the reader unclear about the rationale behind certain conclusions.
4. The logic to draw certain conclusions was confusing and misleading.
   • For instance, the role of orb2 in SELTM is examined via knockdown in MB Kenyon cells (KCs) (using ok107>orb2-RNAi), which is irrelevant to the claim that orb2 functions in YL neurons. Additionally, RNAseq analyses (Fig. 1N-S) focusing on orb2 expression in a/b KCs are irrelevant to and cannot support the claim that Orb2 functions in YL neurons.
   • Similarly, the claim (lines 302-303) that sNPF-R expression is exclusive to MB KCs conflicts with data showing effects when sNPF-R is knocked down in YL neurons. How can knocking-down a gene, which is exclusively expressed in neural population A, in neural population B affect a phenotype? This inconsistency undermines the interpretation of the results.
   • Other examples include lines 223-227 and lines 246-249. It is very confusing how the authors came to the indications.
   • The authors also kept confusing the readers and themselves by mistakenly referring to MB KC a-lobe and YL a-lobe projection. They may know the difference between the two neural populations but they did not always refer to the right one in the text.
5. The imaging figures provided are unfocused and poorly resolved, making it difficult to assess data quality.
   • Colocalization analyses of orb2 and YL are unconvincing, especially given that orb2 is well-documented in literature as expressed in MB a-KCs and YL projection wrapping MB a-lobe. Maximum intensity projection images are insufficient for confirming colocalization; complete image stacks with staining of orb2, YL, and KCs (MB-dsRed) are needed for validation.
   • Quantification of imaging data appears flawed. For example, claims of orb2 and CaMKII upregulation in MB a-lobe projections (e.g., Fig. S2F-J, Fig. 3M,N) are confounded by widespread increases in intensity across the brain, lacking specificity.
   • The TRIC experiment analysis should normalize GFP signals to internal reference channel (RFP in the TRIC construct), as per established protocols in the original paper.
   • In Fig. 6H-J, methods for counting synapse numbers are not described. How are synapse numbers counted in these low-resolution images?
6. The study presents data from unrelated learning paradigms (e.g., olfactory associative learning, courtship conditioning; Fig. 7) without justifying how these paradigms relate to SELTM. Particularly, the authors claimed that SELTM is related to Gr5a, which leads to appetitive memories, which involve PAM dopaminergic neurons and MB horizontal lobes. However, the olfactory associative learning with electric shock and courtship conditioning lead to aversive memories, that involve PPL1 dopaminergic neurons and the vertical lobes.
7. Some figures are not referred to in the text. For example, Fig S1 K and L (also, what's the difference between these two figures?) and Fig 3M-R. What is MB-V3 in Fig 4J-K?

Minor issues

1. Fig 2F. YL projections are labeled as MBONs. Clarify whether YL neurons are the upstream or downstream (MBON) of KCs.
2. Extensive language polishing is required, as several sentences are unclear (e.g., lines 169-172).

Significance

This study potentially advances our understanding of how sexual experience modifies future mating behaviors. While previous work has shown that mating induces appetitive memory in males, the mechanisms linking this memory to future mating behavior remain poorly understood. This work could provide valuable insights into these mechanisms, pending appropriate revisions.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

Summary: 

In this manuscript, the authors explore the role of the conserved transcription factor POU4-2 in planarian maintenance and regeneration of mechanosensory neurons. The authors explore the role of this transcription factor and identify potential targets of this transcription factor. Importantly, many genes discovered in this work are deeply conserved, with roles in mechanosensation and hearing, indicating that planarians may be a useful model with which to study the roles of these key molecules. This work is important within the field of regenerative neurobiology, but also impactful for those studying the evolution of the machinery that is important for human hearing. 

Strengths: 

The paper is rigorous and thorough, with convincing support for the conclusions of the work. 

Weaknesses: 

Weaknesses are relatively minor and could be addressed with additional experiments or changes in writing.

Reviewer #2 (Public review): 

Summary: 

In this manuscript, the authors investigate the role of the transcription factor Smed-pou4-2 in the maintenance, regeneration, and function of mechanosensory neurons in the freshwater planarian Schmidtea mediterranea. First, they characterize the expression of pou4-2 in mechanosensory neurons during both homeostasis and regeneration, and examine how its expression is affected by the knockdown of soxB1, 2, a previously identified transcription factor essential for the maintenance and regeneration of these neurons. Second, the authors assess whether pou4-2 is functionally required for the maintenance and regeneration of mechanosensory neurons. 

Strengths: 

The study provides some new insights into the regulatory role of pou4-2 in the differentiation, maintenance, and regeneration of ciliated mechanosensory neurons in planarians. 

Weaknesses: 

The overall scope is relatively limited. The manuscript lacks clear organization, and many of the conclusions would benefit from additional experiments and more rigorous quantification to enhance their strength and impact. 

Reviewing Editor Comments: 

(1) Quantification of pou4-2(+) cells that express (or do not express) hmcn-1-L and/or pkd1L-2(-) is a common suggestion amongst reviewers. It is recognized that Ross et al. (2018) showed that pkd1L-2 and hmcn-1L expression is detected in separate cells by double FISH, and the analysis presented in Supplementary Figure S3 is helpful in showing that some cells expressing pou4-2 (magenta) are not labeled by the combined signal of pkd1L-2 and hmcn-1-L riboprobes (green). However, I am not sure that we can conclude that pkd1L-2 and hmcn-1-L are effectively detected when riboprobes are combined in the analysis. Therefore, quantification of labeled cells as proposed by Reviewers 1 and 2 would help.

Combining riboprobes is a standard approach in the field, and we chose this method as a direct way to determine which cells lack expression of both genes. We agree that providing the raw quantification data would be helpful for readers, and we included this data in Supplementary File S7; the file contains the quantification information for this dFISH experiment represented in Supplementary Figure 3.

(2) It may be helpful to comment on changes (or lack of changes) in atoh gene RNA levels in RNAseq analyses of pou4-2 animals. As mentioned by one of the reviewers, in situs that don't show signal are inconclusive in this regard. 

We fully agree with both reviewers. Two of the planarian atonal homologs are difficult to detect and produce background signals, which we attempted and previously reported in Cowles et al. Development (2013). We conceived performing reciprocal RNAi/in situ experiments, born out of curiosity given the reported role of atonal in the pou4 cascade in other organisms. However, these exploratory experiments lacked a strong rationale for inclusion, particularly given that pou4-2 and the atonal homologs do not share expression patterns, co-expression, or differential expression in our RNA-seq dataset. Therefore, we decided to omit the atonal in situs following pou4-2 RNAi. We retained the experiments showing that knockdown of the atonal genes does not show robust effects on the mechanosensory neuron pattern, as expected. We thank the reviewing editor and reviewers for pinpointing the concern. We agree that additional experiments, such as qPCR experiments, would be needed. We reasoned that while these additional experiments could be informative, they are unlikely to alter the key conclusions of this study substantially.

(3) There seem to be typos at bottom of Figure 10 and top of page 11 when referencing to Figure 4B (should be to 5B instead): "While mechanosensory neuronal patterned expression of Eph1 was downregulated after pou4-2 and soxB1-2 inhibition, low expression in the brain branches of the ventral cephalic ganglia persisted (Figure 4B)." 

Thank you! We have fixed those.

(4) Typo (page 13; kernel?): "...to test to what extent the Pou4 gene regulatory kernel is conserved among these widely divergent animals." 

Regulatory kernels are defined as the minimal sets of interacting genes that drive developmental processes and are the core circuits within a gene regulatory network, but we recognize that this might not be as well known, so we have changed the term to “network” for clarity.

Reviewer #1 (Recommendations for the authors): 

(1) The authors indicate that they are interested in finding out whether POU4-2 is important in the creation of mechanosensory neurons in adulthood as well as in embryogenesis (in other words, whether the mechanism is "reused during adult tissue maintenance and regeneration"). The manuscript clearly shows that planarian POU4 -2 is important in adult neurogenesis in planarians, but there is no evidence presented to show that this is a recapitulation of embryogenesis. Is pou4-2 expressed in the planarian embryo? This might be possible to examine by ISH or through the evaluation of sequencing data that already exists in the literature. 

We agree that these statements should be precise. We have clarified when we make comparisons to the role of Pou4 in sensory system development in other organisms versus its role in the adult planarian. We examined its expression using the existing database of embryonic gene expression. Thanks for hinting at this idea. We performed BLAST in Planosphere (Davies et al., 2017) to cross-reference our clone matching dd_Smed_v6_30562_0_1, which is identical to SMED30002016. The embryonic gene expression for SMED30002016 indicates this gene is expressed at the expected stages given prior knowledge of the timing of organ development in Schmidtea mediterranea (a positive trend begins at Stage 5, with a marked increase by Stage 6 that remains comparable to the asexual expression levels shown). We thank the reviewer for pointing out this oversight. We have incorporated this result in the paper as a Supplementary Figure and discuss how we can only speculate that it has a similar role as we detect in the adult asexual worms.

(2) Can it be determined whether the punctate pou4-2+ cells outside of the stripes are progenitors or other neural cell types? Are there pou4-2+ neurons that are not mechanosensory cell types? Could there be other roles for POU4-2 in the neurogenesis of other cell types? It might help to show percentages of overlap in Figure 4A and discuss whether the two populations add up to 100% of cells. 

These are good questions that arise in part from other statements that need clarification in the text (pointed out by Reviewer 2). We think some of the dorsal pou4-2⁺ might represent progenitor cells undergoing terminal differentiation (see Supplementary Figure 4). We attempted BrdU pulse chase experiments but were not successful in consistently detecting pou4-2 at sufficient levels with our protocol. In response to this helpful comment, we have included this question as a future direction in the revised Discussion. Finally, we have edited our description of the expression pattern. We already pointed out that there are other cells on the ventral side that are not affected when soxB1-2 is knocked down. We attempted to resolve the potential identity of those cells working with existing scRNA-seq data in collaboration with colleagues, but their low abundance made it difficult to distinguish other populations. While we acknowledge this interesting possibility, we have chosen to focus this report on the role of pou4-2 downstream of soxB1-2, as this represents the most well-supported aspect of the dataset and was positively highlighted by both the reviewer and editor.

(3) The authors discuss many genes from their analysis that play conserved roles in mechanosensation and hearing. Were there any conserved genes that came up in the analysis of pou4-2(RNAi) planarians that have not yet been studied in human hearing and neurodevelopment? I am wondering the extent to which planarians could be used as a discovery system for mechanosensory neuron function and development, and discussion of this point might increase the impact of this paper or provide critical rationale for expanding work on planarian mechanosensation. 

Indeed, we agree that planarians could be used to identify conserved genes with roles in mechanosensation and have included this point in the Discussion. In this study, we have focused on demonstrating the conservation of gene regulation. While this study was initially based on a graduate thesis project, we have since generated a more comprehensive dataset from isolated heads, which we are currently analyzing. This has been emphasized in the revised Discussion.

Minor: 

(1) For Figure 6E, the authors could consider showing data along a negative axis to indicate a decrease in length in response to vibration and to more clearly show that this decrease doesn't occur as strongly after pou4-2(RNAi). 

We displayed this behavior as the percent change, as this is a standard way to represent this data. As the percent change is a positive value, we represent the data as these positive values.

(2) The authors should consider quantifying the decrease of pou4-2 mRNA after atonal(RNAi) conditions, either by RT-qPCR or cell quantification. Visually, the signal in the stripes after atoh8-2(RNAi) seems lower, particularly in the tail. The punctate pattern outside the stripes may also be decreased after atoh8-1(RNAi). But quantification might strengthen the argument. 

We agree with the reviewer and acknowledge that we should have been more cautious in interpreting these results. Those two genes are difficult to detect and did not show specific patterns in Cowles et al. (2013). The reviewer is correct that additional experiments are necessary before reaching conclusions, but we do not think as discussed earlier we do not think new experiments would provide insights for the major conclusions. These experiments were exploratory in nature and tangential to our main conclusions, especially in the absence of reciprocal evidence (e.g., shared expression patterns, co-expression, or differential expression in our RNA-seq data. Therefore, we decided to eliminate the atonal in situs following pou4-2 RNAi.

Reviewer #2 (Recommendations for the authors): 

A. Expression of pou4-2 in ciliated mechanosensory neurons: 

(1) The conclusion that pou4-2 is expressed in ciliated mechanosensory neurons is primarily based on co-expression analysis using a published single-cell dataset. Although the authors later show that a subset of pou4-2 cells also express pkd1L-2 (Figure 4A), a known marker of ciliated mechanosensory neurons, this finding is not properly quantified. I recommend moving Figure 4A to earlier in the manuscript (e.g., to Figure 2) and expanding the analysis to include additional known markers of this cell type. Proper quantification of the extent of co-localization is necessary to support the claim robustly. 

As pointed out by the reviewer, there is substantive evidence from our lab and other reports. King et al. also showed pou4-2 and pkd1L-2 ‘regulation’ by their scRNA-seq data, and this function is conserved in the acoel Hofstenia miamia (Hulett et al., PNAS 2024 ). Our analysis shows convincing co-localization by scRNA-seq and expression of soxB1-2 and neural markers in the respective populations. Furthermore, we included colocalization of pou4-2 with mechanosensory genes using fluorescence in situ hybridization (Figure 3B, Supplementary Figure 4, and Supplementary File S7). We are confident the data conclusively show pou4-2 regulates pkd1L-2 expression in a subset of mechanosensory neurons. Given the strength of existing observations and previously published data, we believe that additional staining experiments are not essential to support this conclusion. 

(2) There appears to be a conceptual inconsistency in the interpretation of pou4-2 expression dynamics. On one hand, the authors suggest that delayed pou4-2 expression indicates a role in late-stage differentiation (p.6). On the other hand, they propose that pou4-2 may be expressed in undifferentiated progenitors to initiate downstream transcriptional programs (p.8). These interpretations should be reconciled. Additionally, claims regarding pou4-2 expression in progenitor populations should be supported by co-localization with established stem cell or progenitor markers, rather than inferred from signal intensity alone. 

This is an excellent point, and we agree with the reviewer that this section requires editing. As described in response to Reviewer 1, we attempted BrdU pulse chase experiments but were not successful in consistently detecting pou4-2 at sufficient levels with our protocol. Furthermore, we could not obtain strong signals in double labeling experiments in pou4-2 in situs combined with piwi-1 or PIWI-1 antibodies. We will include those experiments as a future direction and amend our conclusions accordingly.

(3) The expression pattern shown in Figure 1B raises questions about the precise anatomical localization of pou4-2 cells. It is unclear whether these cells reside in the subepidermal plexus or the deeper submuscular plexus, which represent distinct neuronal layers (Ross et al., 2017). The observed signals near the ventral nerve cords could suggest submuscular localization. To clarify this, higher-resolution imaging and co-staining with region-specific neural markers are recommended. 

In Ross et al. (2018), we showed that the pkd1L-2⁺ cells are located submuscularly. The pkd1L-2 cells express pou4-2, thus the pou4-2⁺ cells are located in the same location. Based on co-expression data and co-expression with PKD genes, we are confident it is submuscular.

B. The functional requirements of pou4-2 in the maintenance of mechanosensory neurons: 

(1) To evaluate the functional role of pou4-2 in maintaining mechanosensory neurons, the authors performed whole-animal RNA-seq on pou4-2(RNAi) and control animals, identifying a significant downregulation of genes associated with mechanosensory neuron expression. However, the presentation of these findings is fragmented across Figures 3, 4, and 5. I recommend consolidating the RNA-seq results (Figure 3) and the subsequent validation of downregulated genes (Figures 4 and 5) into a single, cohesive figure. This would improve the logical flow and clarity of the manuscript. 

As suggested by the reviewer, we have combined Figures 3 and 4 (new Figure 3), which we believe improves the flow. We decided to keep Figure 5 (new Figure 4) as a standalone because it focuses on the characterization of new genes revealed by RNAseq and scRNA-seq data mining that were not previously reported in Ross et al. 2018 and

2024.

(2) In pou4-2(RNAi) animals, pkd1L-2 expression appears to be entirely lost, while hmcn-1-L shows faint expression in scattered peripheral regions. The authors suggest that an extended RNAi treatment might be necessary to fully eliminate hmcn-1-L expression. However, an alternative explanation is that pou4-2 is not essential for maintaining all hmcn-1-L cells, particularly if pou4-2 expression does not fully overlap with that of hmcn-1-L. This possibility should be acknowledged and discussed. 

We agree and have acknowledged this point in the revised text.

(3) On page 9, the section title claims that "Smed-pou4-2 regulates genes involved in ciliated cell structure organization, cell adhesion, and nervous system development." While some differentially expressed genes are indeed annotated with these functions based on homology, the manuscript does not provide experimental evidence supporting their roles in these biological processes in planarians. The title should be revised to avoid overstatement, and the limitations of extrapolating a function solely from gene annotation should be acknowledged. 

Excellent point. We have edited the text to indicate that the genes were annotated or implicated.

(4) The cilia staining presented in Figure 6B to support the claim that pou4-2 is required for ciliated cell structure organization is unconvincing. Improved imaging and more targeted analysis (e.g., co-labeling with mechanosensory markers) are needed to support this conclusion. 

We have addressed this concern by adjusting the language to be more precise and indicate that the stereotypical banded pattern is disrupted with decreased cilia labeling along the dorsal ciliated stripe. Indeed, our conclusion overstated the observations made with the staining and imaging resolution. Thank you.

C. The functional requirements of pou4-2 in the regeneration of mechanosensory neurons: 

To evaluate the role of pou4-2 in the regeneration of mechanosensory neurons, the authors performed amputations on pou4-2(RNAi) and control(RNAi) animals and assessed the expression of mechanosensory markers (pkd1L-2, hmcn-1-L) alongside a functional assay. However, the results shown in Figure 4B indicate the presence of numerous pkd1L-2 and hmcn-1-L cells in the blastema of pou4-2(RNAi) animals. This observation raises the possibility that pou4-2 may not be essential for the regeneration of these mechanosensory neurons. The authors should address this alternative interpretation. 

Our interpretation is that there were very few cells expressing the markers compared to controls. The pattern was predominantly lost, which is consistent with other experiments shown in the paper. However, we have added the additional caveat suggested by the reviewer.

Minor points: 

(1) On p.8, the authors wrote "every 12 hours post-irradiation". However, this is not consistent with the figure, which only shows 0, 3, 4, 4.5, 5, and 5.5 dpi. 

We corrected this. Thank you for catching the mistake!

(2) On p.12, the authors wrote "Analysis of pou4-2 RNAi data revealed differentially expressed genes with known roles in mechanosensory functions, such as loxhd-1, cdh23, and myo7a. Mutations in these genes can cause a loss of mechanosensation/transduction". This is misleading because, to my knowledge, the role of these genes in planarians is unknown. If the authors meant other model systems, they should clearly state this in the text and include proper references. 

The reviewer is correct that we are referencing findings from other organisms. We have clarified this point in the revised text. The appropriate references were included and cited in the first version.

(3) On p.7, the authors wrote, "conversely, the expression of atonal genes was unaffected in pou4-2 RNAi-treated regenerates (Supplementary Figure S2B)". However, it is unclear whether the Atoh8-1 and Atoh8-2 signals are real, as the quality of the in situ results is too low to distinguish between real signals and background noise/non-specific staining. 

This valid concern was addressed in our response to Reviewer 1. We have adjusted the figure and the text accordingly.

(4) On p.6 the authors wrote "pinpointed time points wherein the pou4-2 transcripts were robustly downregulated". However, the current version of the manuscript does not provide data explaining why Pou4-2 transcripts are robustly downregulated on day 12. 

Yes, we determined the appropriate time points using qPCR for all sample extractions. As an example, see the figure for qPCR validation at day 12 showing that pou4-2 and pkd1L2 are down.

Author response image 1.

In this graph, samples labeled “G” represent four biological controls of gfp(RNAi) control animals, and samples labeled “P” represent four biological controls of pou4-2(RNAi)animals at day 12 in the RNAi protocol.

(5) On p.13, the authors wrote "collecting RNA from how animals." Is this a typo? 

Thanks for catching the typo. It should read “whole” animals. We have corrected this.

(6) On p.14, the authors wrote "but the expression patterns of planarian atonal genes indicated that they represent completely different cell populations from pou4-2-regulated mechanosensory neurons". However, this is unclear from the images, as the in situ staining of Atoh8-1 and Atoh82 are potentially failed stainings. 

We agree. We have edited accordingly.

Author response:

The following is the authors’ response to the original reviews

Public Reviews

Reviewer #1 (Public review):

Summary:

The authors performed genome assemblies for two Fagaceae species and collected transcriptome data from four natural tree species every month over two years. They identified seasonal gene expression patterns and further analyzed species-specific differences.

Strengths:

The study of gene expression patterns in natural environments, as opposed to controlled chambers, is gaining increasing attention. The authors collected RNA-seq data monthly for two years from four tree species and analyzed seasonal expression patterns. The data are novel. The authors could revise the manuscript to emphasize seasonal expression patterns in three species (with one additional species having more limited data). Furthermore, the chromosome-scale genome assemblies for the two Fagaceae species represent valuable resources, although the authors did not cite existing assemblies from closely related species.

Thank you for your careful assessment of our manuscript.

Weaknesses:

Comment; The study design has a fundamental flaw regarding the evaluation of genetic or evolutionary effects. As a basic principle in biology, phenotypes, including gene expression levels, are influenced by genetics, environmental factors, and their interaction. This principle is well-established in quantitative genetics.

In this study, the four species were sampled from three different sites (see Materials and Methods, lines 543-546), and additionally, two species were sampled from 2019-2021, while the other two were sampled from 2021-2023 (see Figure S2). This critical detail should be clearly described in the Results and Materials and Methods. Due to these variations in sampling sites and periods, environmental conditions are not uniform across species.

Even in studies conducted in natural environments, there are ways to design experiments that allow genetic effects to be evaluated. For example, by studying co-occurring species, or through transplant experiments, or in common gardens. To illustrate the issue, imagine an experiment where clones of a single species were sampled from three sites and two time periods, similar to the current design. RNA-seq analysis would likely detect differences that could qualitatively resemble those reported in this manuscript.

One example is in line 197, where genus-specific expression patterns are mentioned. While it may be true that the authors' conclusions (e.g., winter synchronization, phylogenetic constraints) reflect real biological trends, these conclusions are also predictable even without empirical data, and the current dataset does not provide quantitative support.

If the authors can present a valid method to disentangle genetic and environmental effects from their dataset, that would significantly strengthen the manuscript. However, I do not believe the current study design is suitable for this purpose.

Unless these issues are addressed, the use of the term "evolution" is inappropriate in this context. The title should be revised, and the result sections starting from "Peak months distribution..." should be either removed or fundamentally revised. The entire Discussion section, which is based on evolutionary interpretation, should be deleted in its current form.

If the authors still wish to explore genetic or evolutionary analyses, the pair of L. edulis and L. glaber, which were sampled at the same site and over the same period, might be used to analyze "seasonal gene expression divergence in relation to sequence divergence." Nevertheless, the manuscript would benefit from focusing on seasonal expression patterns without framing the study in evolutionary terms.

We sincerely thank the reviewer for the detailed and thoughtful comments. We fully recognize the importance of carefully distinguishing genetic and environmental contributions in transcriptomic studies, particularly when addressing evolutionary questions. The reviewer identified two major concerns regarding our study design: (1) the use of different monitoring periods across species, and (2) the use of samples collected from different study sites. We addressed both concerns with additional analyses using 112 new samples and now present new evidence that supports the robustness of our conclusions.

(1) Monitoring period variation does not bias our conclusions<br /> To address concerns about the differing monitoring periods, we added new RNA-seq data (42 samples each for bud and leaf samples for L. glaber and 14 samples each for bud and leaf samples for _L. eduli_s) collected from November 2021 to November 2022, enabling direct comparison across species within a consistent timeframe. Hierarchical clustering of this expanded dataset (Fig. S6) yielded results consistent with our original findings: winter-collected samples cluster together regardless of species identity. This strongly supports our conclusion that the seasonal synchrony observed in winter is not an artifact of the monitoring period and demonstrates the robustness of our conclusions across datasets.

(2) Site variation is limited and does not confound our findings<br /> Although the study included three sites, two of them (Imajuku and Ito Campus) are only 7.3 km apart, share nearly identical temperature profiles (see Fig. S2), and are located at the edge of similar evergreen broadleaf forests. Only Q. acuta was sampled from a higher-altitude, cooler site. To assess whether the higher elevation site of Q. acuta introduced confounding environmental effects, we reanalyzed the data after excluding this species. Hierarchical clustering still revealed that winter bud samples formed a distinct cluster regardless of species identity (Fig. S7), consistent with our original finding.

Furthermore, we recalculated the molecular phenology divergence index D (Fig. 4C) and the interspecific Pearson’s correlation coefficients (Fig. 5A) without including Q. acuta. These analyses produced results that were similar to those obtained from the full dataset (Fig. S12; Fig. S14), indicating that the observed patterns are not driven by environmental differences associated with elevation.

(3) Justification for our approach in natural systems<br /> We agree with the reviewer that experimental approaches such as common gardens, reciprocal transplants, and the use of co-occurring species are valuable for disentangling genetic and environmental effects. In fact, we have previously implemented such designs in studies using the perennial herb Arabidopsis halleri (Komoto et al., 2022, https://doi.org/10.1111/pce.14716) and clonal Someiyoshino cherry trees (Miyawaki-Kuwakado et al., 2024, https://doi.org/10.1002/ppp3.10548) to examine environmental effects on gene expression. However, extending these approaches to long-lived tree species in diverse natural ecosystems poses significant logistical and biological challenges. In this study, we addressed this limitation by including three co-occurring species at the same site, which allowed us to evaluate interspecific differences under comparable environmental conditions. Importantly, even when we limited our analyses to these co-occurring species, the results remained consistent, indicating that the observed variation in transcriptomic profiles cannot be attributed to environmental factors alone and likely reflects underlying genetic influences.

Accordingly, we added four new figures (Fig. S6, Fig. S7, Fig. S12 and Fig. S14) and revised the manuscript to clarify the limitations and strengths of our design, to tone down the evolutionary claims where appropriate, and to more explicitly define the scope of our conclusions in light of the data. We hope that these efforts sufficiently address the reviewer’s concerns and strengthen the manuscript.

To better support the seasonal expression analysis, the early RNA-seq analysis sections should be strengthened. There is little discussion of biological replicate variation or variation among branches of the same individual. These could be important factors to analyze. In line 137, the mapping rate for two species is mentioned, but the rates for each species should be clearly reported. One RNA-seq dataset is based on a species different from the reference genome, so a lower mapping rate is expected. While this likely does not hinder downstream analysis, quantification is important.

We thank the reviewer 1 for the helpful comment. To evaluate the variation among biological replicates, we compared the expression level of each gene across different individuals. We observed high correlation between each pair of individuals (Q. glauca (n=3): an average correlation coefficient r = 0.947; Q. acuta (n=3): r = 0.948; L. glaber (n=3): r = 0.948)). This result suggests that the seasonal gene expression pattern is highly synchronized across individuals within the same species. We mentioned this point in the Result section in the revised manuscript. We also calculated the mean mapping rates for each species. As the reviewer expected, the mapping rate was slightly lower in Q. acuta (88.6 ± 2.3%) and L. glaber (84.3 ± 5.4%), whose RNA-Seq data were mapped to reference genomes of related but different species, compared to that in Q. glauca (92.6 ± 2.2%) and L. edulis (89.3 ± 2.7%). However, we minimized the impact of these differences on downstream analysis. These details have been included in the revised main text.

In Figures 2A and 2B, clustering is used to support several points discussed in the Results section (e.g., lines 175-177). However, clustering is primarily a visualization method or a hypothesis-generating tool; it cannot serve as a statistical test. Stronger conclusions would require further statistical testing.

We thank the reviewer for the helpful comment. As noted, we acknowledge that hierarchical clustering (Fig. 2A) is primarily a visualization and hypothesis-generating method. To assess the biological relevance of the clusters identified, we conducted a Mann-Whitney U test or the Steel-Dwass test to evaluate whether the environmental temperatures at the time of sample collection differed significantly among the clusters. This analysis (Fig. 2B) revealed statistically significant differences in temperature in the cluster B3 (p < 0.01), indicating that the gene expression clusters are associated with seasonal thermal variation. These results support the interpretation that the clusters reflect coordinated transcriptional responses to environmental temperature. We revised the Results section to clarify this point.

The quality of the genome assemblies appears adequate, but related assemblies should be cited and discussed. Several assemblies of Fagaceae species already exist, including Quercus mongolica (Ai et al., Mol Ecol Res, 2022), Q. gilva (Front Plant Sci, 2022), and Fagus sylvatica (GigaScience, 2018), among others. Is there any novelty here? Can you compare your results with these existing assemblies?

We agree that genome assemblies of Fagaceae species are becoming increasing available. However, our study does not aim to emphasize the novelty of the genome assemblies per se. Rather, with the increasing availability of chromosome-level genomes, we regard genome assembly as a necessary foundation for more advanced analyses. The main objective of our study is to investigate how each gene is expressed in response to seasonal environmental changes, and to link genome information with seasonal transcriptomic dynamics. To address the reviewer’s comment in line with this objective, we added a discussion on the syntenic structure of eight genome assemblies spanning four genera within the Fagaceae, including a species from the genus Fagus (Ikezaki et al. 2025, https://doi.org/10.1101/2025.07.31.667835). This addition helps to position our work more clearly within the context of existing genomic resources.

Most importantly, Figure 1B-D shows synteny between the two genera but also indicates homology between different chromosomes. Does this suggest paleopolyploidy or another novel feature? These chromosome connections should be interpreted in the main text-even if they could be methodological artifacts.

A previous study on genome size variation in Fagaceae suggested that, given the consistent ploidy level across the family, genome expansion likely occurred through relatively small segmental duplications rather than whole-genome duplications. Because Figure 1B-D supports this view, we cited the following reference in the revised version of the manuscript. Chen et al. (2014) https://doi.org/10.1007/s11295-014-0736-y

In both the Results and Materials and Methods sections, descriptions of genome and RNA-seq data are unclear. In line 128, a paragraph on genome assembly suddenly introduces expression levels. RNA-seq data should be described before this. Similarly, in line 238, the sentence "we assembled high-quality reference genomes" seems disconnected from the surrounding discussion of expression studies. In line 632, Illumina short-read DNA sequencing is mentioned, but it's unclear how these data were used.

We relocated the explanation regarding the expression levels of single-copy and multi-copy genes to the section titled “Seasonal gene expression dynamics.” Additionally, we clarified in the Materials and Methods section that short-read sequencing data were used for both genome size estimation and phylogenetic reconstruction.

Reviewer #2 (Public review):

Summary:

This study explores how gene expression evolves in response to seasonal environments, using four evergreen Fagaceae species growing in similar habitats in Japan. By combining chromosome-scale genome assemblies with a two-year RNA-seq time series in leaves and buds, the authors identify seasonal rhythms in gene expression and examine both conserved and divergent patterns. A central result is that winter bud expression is highly conserved across species, likely due to shared physiological demands under cold conditions. One of the intriguing implications of this study is that seasonal cycles might play a role similar to ontogenetic stages in animals. The authors touch on this by comparing their findings to the developmental hourglass model, and indeed, the recurrence of phenological states such as winter dormancy may act as a cyclic form of developmental canalization, shaping expression evolution in a way analogous to embryogenesis in animals.

Strengths:

(1) The evolutionary effects of seasonal environments on gene expression are rarely studied at this scale. This paper fills that gap.

(2) The dataset is extensive, covering two years, two tissues, and four tree species, and is well suited to the questions being asked.

(3) Transcriptome clustering across species (Figure 2) shows strong grouping by season and tissue rather than species, suggesting that the authors effectively controlled for technical confounders such as batch effects and mapping bias.

(4) The idea that winter imposes a shared constraint on gene expression, especially in buds, is well argued and supported by the data.

(5) The discussion links the findings to known concepts like phenological synchrony and the developmental hourglass model, which helps frame the results.

We are grateful for the reviewer for the detailed and thoughtful review of our manuscript.

Weaknesses:

(1) While the hierarchical clustering shown in Figure 2A largely supports separation by tissue type and season, one issue worth noting is that some leaf samples appear to cluster closely with bud samples. The authors do not comment on this pattern, which raises questions about possible biological overlap between tissues during certain seasonal transitions or technical artifacts such as sample contamination. Clarifying this point would improve confidence in the interpretation of tissue-specific seasonal expression patterns.

Leaf samples clustered into the bud are newly flushed leaves collected in April for Q. glauca, May for Q. acuta, May and June for L. edulis, and August and September for L. glaber. To clarify this point, we highlighted these newly flushed leaf samples as asterisk in the revised figure (Fig. 2A).

(2) While the study provides compelling evidence of conserved and divergent seasonal gene expression, it does not directly examine the role of cis-regulatory elements or chromatin-level regulatory architecture. Including regulatory genomic or epigenomic data would considerably strengthen the mechanistic understanding of expression divergence.

We thank the reviewer for this insightful comment. As noted in the Discussion section, we hypothesize that such genome-wide seasonal expression patterns—and their divergence across species—are likely mediated by cis-regulatory elements and chromatin-level mechanisms. While a direct investigation of regulatory architecture was beyond the scope of the present study, we fully agree that incorporating regulatory genomic and epigenomic data would significantly deepen the mechanistic understanding of expression divergence. In this regard, we are currently working to identify putative cis-regulatory elements in non-coding regions and are collecting epigenetic data from the same tree species using ChIP-seq. We believe the current study provide a foundation for these future investigations into the regulatory basis of seasonal transcriptome variation. We made a minor revision to the Discussion to note that an important future direction is to investigate the evolution of non-coding sequences that regulate gene expression in response to seasonal environmental changes.

(3) The manuscript includes a thoughtful analysis of flowering-related genes and seasonal GO enrichment (e.g., Figure 3C-D), providing an initial link between gene expression timing and phenological functions. However, the analysis remains largely gene-centric, and the study does not incorporate direct measurements of phenological traits (e.g., flowering or bud break dates). As a result, the connection between molecular divergence and phenotypic variation, while suggestive, remains indirect.

We would like to note that phenological traits have been observed in the field on a monthly basis throughout the sampling period and the phenological data were plotted together with molecular phenology (e.g. Fig. 2A, C; Fig. 3C, D). Although the temporal resolution is limited, these observations captured species-specific differences in key phenological events such as leaf flushing and flowering times. We revised the manuscript to clarify this point.

(4) Although species were sampled from similar habitats, one species (Q. acuta) was collected at a higher elevation, and factors such as microclimate or local photoperiod conditions could influence expression patterns. These potential confounding variables are not fully accounted for, and their effects should be more thoroughly discussed or controlled in future analyses.

We fully agree with the reviewer that local environmental conditions, including microclimate and photoperiod differences, could potentially influence gene expression patterns. To assess whether the higher elevation site of Q. acuta introduced confounding environmental effects, we reanalyzed the data after excluding this species. Hierarchical clustering still revealed that winter bud samples formed a distinct cluster regardless of species identity (Fig. S7), consistent with our original finding.

Furthermore, we recalculated the molecular phenology divergence index D (Fig. 4C) and the interspecific Pearson’s correlation coefficients (Fig. 5A) without including Q. acuta. These analyses produced results that were qualitatively similar to those obtained from the full dataset (Fig. S12; Fig. S14), indicating that the observed patterns are not driven by environmental differences associated with elevation.

We believe these additional analyses help to decouple the effects of environment and genetics, and support our conclusion that both seasonal synchrony and phylogenetic constraints play key roles in shaping transcriptome dynamics. We added four new figures (Fig. S6, Fig. S7, Fig. S12 and Fig. S14) and revised the text accordingly to clarify this point and to acknowledge the potential impact of site-specific environmental variation.

(5) Statistical and Interpretive Concerns Regarding Δφ and dN/dS Correlation (Figures 5E and 5F):

a) Statistical Inappropriateness: Δφ is a discrete ordinal variable (likely 1-11), making it unsuitable for Pearson correlation, which assumes continuous, normally distributed variables. This undermines the statistical validity of the analysis.

We thank the reviewer for the insightful comment. We would like to clarify that the analysis presented in Figures 5E and 5F was based on linear regression, not Pearson’s correlation. Although Δ_φ_ is a discrete variable, it takes values from 0 to 6 in 0.5 increments, resulting in 13 levels. We treated it as a quasi-continuous variable for the purposes of linear regression analysis. This approach is commonly adopted in practice when a discrete variable has sufficient resolution and ordering to approximate continuity. To enhance clarity, we revised the manuscript to explicitly state that linear regression was used, and we now reported the regression coefficient and associated p-value to support the interpretation of the observed trend.

b) Biological Interpretability: Even with the substantial statistical power afforded by genome-wide analysis, the observed correlations are extremely weak. This suggests that the relationship, if any, between temporal divergence in expression and protein-coding evolution is negligible.

Taken together, these issues weaken the case for any biologically meaningful association between Δφ and dN/dS. I recommend either omitting these panels or clearly reframing them as exploratory and statistically limited observations.

We agree with the reviewer’s comment. While we retained the original panels, we reframed our interpretation to emphasize that, despite statistical significance, the observed correlation is very weak—suggesting that coding region variation is unlikely to be the primary driver of seasonal gene expression patterns. Accordingly, we revised the “Relating seasonal gene expression divergence to sequence divergence” section in the Results, as well as the relevant part of the Discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Sentences around lines 250-251 are incomplete and need revision.

We thank the reviewer for pointing this out. We revised the sentences in the subsection “Peak month distribution of rhythmic genes and intra-genus and inter-genera comparison” in the Results section to ensure clarity and completeness. In addition, to improve the interpretability of the peak month distribution, we added arrows to indicate the major peaks in the circular histograms shown in Fig. 3C and 3D.

Reviewer #2 (Recommendations for the authors):

(1) In Figure 1E-G, the term Copy number or Copy number variation could be misleading, as it is commonly associated with inter-individual gene copy number variation in a population. Since the analysis here refers to orthology relationships rather than population-level variation, a more precise term, such as orthogroup classification, may be preferable.

We thank the reviewer for this helpful suggestion. We agree that the term “copy number” could be misleading in this context. Accordingly, we updated the labeling in Fig. 1 to reflect the more precise term “orthogroup classification.”

(2) In Figure 3A, the x-axis label Period (month) may be misleading, as it could be mistaken for calendar months rather than referring to the periodicity of gene expression cycles. A more explicit label, such as Expression periodicity (months), might improve clarity for the reader.

We thank the reviewer for this valuable suggestion. In the original version of Fig. 3A, we used the label “Period (month),” which could indeed be misinterpreted as referring to calendar months. To clarify that this axis represents the length of gene expression cycles, we revised the label to “Period length (months).” This change also aligns with the terminology used throughout the manuscript, where “Period” refers specifically to cycle length, and “Periodicity” denotes the presence or absence of rhythmic expression.

Other minor revisions

We also made minor revisions for the reference list and the grant number details, and included the accession numbers for all DNA and RNA sequence data deposited in the DNA Data Bank of Japan (DDBJ) in the Data deposition and code availability section, in addition to the BioProject ID.

Author Response:

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

Reviewer #1 (Public review):

The scale bar for fly and ovary images should be included in Figures 9, 10, and 12.

We agree with this comment and apologize for the oversight. We have now modified Figures 9, 10, and 12 to include the scale bars for the ovary images. The fly images were acquired using a stereo microscope where scale bar calculation was not possible. However, all images were acquired at the same magnification for consistency.

Reviewer #2 (Public review):

A weakness of this paper is the phylogenetic analysis to investigate if there is correspondence in the phylogenetic distribution of ITP-type and Gyc76C-type genes/proteins. Unfortunately, the evidence presented is rather limited in scope. Essentially, the authors report that they only found ITP-type and Gyc76C-type genes/proteins in protostomes, but not in deuterostomes. What is needed is a more fine-grained analysis at the species level within the protostomes. However, I recognise that such a detailed analysis may extend beyond the scope of this paper, which is already rich in data.

We thank the reviewer for their comment and the suggestion to perform a fine-grained species level comparison of ITP and Gyc76C genes across protostomes. We are unsure of the utility of this analysis for the present study given that we have now shown that ITPa can activate Gyc76C using both an ex vivo and a heterologous assay, the latter being the gold standard in GPCR and guanylate cyclase discovery (see Huang et al 2025 https://doi.org/10.1073/pnas.2420966122; Beets et al 2023 https://doi.org/10.1016/j.celrep.2023.113058); Chang et al 2009 https://doi.org/10.1073/pnas.0812593106.

Additionally, absence of a gene in a genome/proteome is hard to prove especially when many/most of the protostomian datasets are not as high-quality as those of model systems (e.g. Drosophila melanogaster and Caenorhabditis elegans). Secondly, based on previous findings in Bombyx mori (Nagai et al. 2014 https://doi.org/10.1074/jbc.m114.590646 and Nagai et al. 2016 https://doi.org/10.1371/journal.pone.0156501) and Drosophila (Xu et al. 2023 https://doi.org/10.1038/s41586-023-06833-8 and our study) it is evident that different products of the ITP gene (ITPa and ITPL) could signal via different receptor types depending on the species. Hence, we would need to explore the presence of several genes (ITP, tachykinin, pyrokinin, tachykinin receptor, pyrokinin receptor, CG30340 orphan receptor and Gyc76C) to fully understand which components of these diverse signaling systems are present in a given species to decipher the potential for cross-talk.

While this species-level comparison will certainly be useful in the context of ITP-Gyc76C evolution, it will not alter the conclusions of the present study – ITPa acts via Gyc76C in Drosophila. We therefore agree with the reviewer that these analyses are beyond the scope of this paper.

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

Reviewer #1 (Public Review):  

Summary:  

In Drosophila melanogaster, ITP has functions on feeding, drinking, metabolism, excretion, and circadian rhythm. In the current study, the authors characterized and compared the expression of all three ITP isoforms (ITPa and ITPL1&2) in the CNS and peripheral tissues of Drosophila. An important finding is that they functionally characterized and identified Gyc76C as an ITPa receptor in Drosophila using both in vitro and in vivo approaches. In vitro, the authors nicely confirmed that the inhibitory function of recombinant Drosophila ITPa on MT secretion is Gyc76C-dependent (knockdown Gyc76C specifically in two types of cells abolished the anti-diuretic action of Drosophila ITPa on renal tubules). They also used a combination of multiple approaches to investigate the roles of ITPa and Gyc76C on osmotic and metabolic homeostasis modulation in vivo. They revealed that ITPa signaling to renal tubules and fat body modulates osmotic and metabolic homeostasis via Gyc76C.  

Furthermore, they tried to identify the upstream and downstream of ITP neurons in the nervous system by using connectomics and single-cell transcriptomic analysis. I found this interesting manuscript to be well-written and described. The findings in this study are valuable to help understand how ITP signals work on systemic homeostasis regulation. Both anatomical and single-cell transcriptome analysis here should be useful to many in the field. 

We thank this reviewer for the positive and thorough assessment of our manuscript.  

Strengths:  

The question (what receptors of ITPa in Drosophila) that this study tries to address is important. The authors ruled out the Bombyx ITPa receptor orthologs as potential candidates. They identified a novel ITP receptor by using phylogenetic, anatomical analysis, and both in vitro and in vivo approaches. 

The authors exhibited detailed anatomical data of both ITP isoforms and Gyc76C (in the main and supplementary figures), which helped audiences understand the expression of the neurons studied in the manuscript.  

They also performed connectomes and single-cell transcriptomics analysis to study the synaptic and peptidergic connectivity of ITP-expressing neurons. This provided more information for better understanding and further study on systemic homeostasis modulation.  

Weaknesses:  

In the discussion section, the authors raised the limitations of the current study, which I mostly agree with, such as the lack of verification of direct binding between ITPa and Gyc76C, even though they provided different data to support that ITPa-Gyc76C signaling pathway regulates systemic homeostasis in adult flies. 

We now provide evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Reviewer #2 (Public Review):  

Summary:  

The physiology and behaviour of animals are regulated by a huge variety of neuropeptide signalling systems. In this paper, the authors focus on the neuropeptide ion transport peptide (ITP), which was first identified and named on account of its effects on the locust hindgut (Audsley et al. 1992). Using Drosophila as an experimental model, the authors have mapped the expression of three different isoforms of ITP (Figures 1, S1, and S2), all of which are encoded by the same gene.  

The authors then investigated candidate receptors for isoforms of ITP. Firstly, Drosophila orthologs of G-protein coupled receptors (GPCRs) that have been reported to act as receptors for ITPa or ITPL in the insect Bombyx mori were investigated. Importantly, the authors report that ITPa does not act as a ligand for the GPCRs TkR99D and PK2-R1 (Figure S3). Therefore, the authors investigated other putative receptors for ITPs. Informed by a previously reported finding that ITP-type peptides cause an increase in cGMP levels in cells/tissues (Dircksen, 2009, Nagai et al., 2014), the authors investigated guanylyl cyclases as candidate receptors for ITPs. In particular, the authors suggest that Gyc76C may act as an ITP receptor in Drosophila.  

Evidence that Gyc76C may be involved in mediating effects of ITP in Bombyx was first reported by Nagai et al. (2014) and here the authors present further evidence, based on a proposed concordance in the phylogenetic distribution ITP-type neuropeptides and Gyc76C (Figure 2). Having performed detailed mapping of the expression of Gyc76C in Drosophila (Figures 3, S4, S5, S6), the authors then investigated if Gyc76C knockdown affects the bioactivity of ITPa in Drosophila. The inhibitory effect of ITPa on leucokinin- and diuretic hormone-31-stimulated fluid secretion from Malpighian tubules was found to be abolished when expression of Gyc76C was knocked down in stellate cells and principal cells, respectively (Figure 4). However, as discussed below, this does not provide proof that Gyc76C directly mediates the effect of ITPa by acting as its receptor. The effect of Gyc76C knockdown on the action of ITPa could be an indirect consequence of an alteration in cGMP signalling.  

Having investigated the proposed mechanism of ITPa in Drosophila, the authors then investigated its physiological roles at a systemic level. In Figure 5 the authors present evidence that ITPa is released during desiccation and accordingly, overexpression of ITPa increases survival when animals are subjected to desiccation. Furthermore, knockdown of Gyc76C in stellate or principal cells of Malphigian tubules decreases survival when animals are subject to desiccation. However, whilst this is correlative, it does not prove that Gyc76C mediates the effects of ITPa. The authors investigated the effects of knockdown of Gyc76C in stellate or principal cells of Malphigian tubules on i). survival when animals are subject to salt stress and ii). time taken to recover from of chill coma. It is not clear, however, why animals overexpressing ITPa were also not tested for its effect on i). survival when animals are subject to salt stress and ii). time taken to recover from of chill coma. In Figures 6 and S8, the authors show the effects of Gyc76C knockdown in the female fat body on metabolism, feeding-associated behaviours and locomotor activity, which are interesting. Furthermore, the relevance of the phenotypes observed to potential in vivo actions of ITPa is explored in Figure 7. The authors conclude that "increased ITPa signaling results in phenotypes that largely mirror those seen following Gyc76C knockdown in the fat body, providing further support that ITPa mediates its effects via Gyc76C." Use of the term "largely mirror" seems inappropriate here because there are opposing effects- e.g. decreased starvation resistance in Figure 6A versus increased starvation resistance in Figure 7A. Furthermore, as discussed above, the results of these experiments do not prove that the effects of ITPa are mediated by Gyc76C because the effects reported here could be correlative, rather than causative. 

We thank this reviewer for an extremely thorough and fair assessment of our manuscript. 

We have now performed salt stress tolerance and chill coma recovery assays using flies over-expressing ITPa (new Figure 10 Supplement 1).

We agree that the use of the term “largely mirrors” to describe the effects of ITPa overexpression and Gyc76C knockdown is not appropriate and have changed this sentence. We also agree that the experiments did not provide direct evidence that the effects of ITPa are mediated by Gyc76C. To address this, we now provide evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Lastly, in Figures 8, S9, and S10 the authors analyse publicly available connectomic data and single-cell transcriptomic data to identify putative inputs and outputs of ITPa-expressing neurons. These data are a valuable addition to our knowledge ITPa expressing neurons; but they do not address the core hypothesis of this paper - namely that Gyc76C acts as an ITPa receptor.  

The goal of our study was to comprehensively characterize an anti-diuretic system in Drosophila. Hence, in addition to identifying the receptor via which ITPa exerts its effects, we also wanted to understand how ITPa-producing neurons are regulated. Connectomic and single-cell transcriptomic analyses are highly appropriate for this purpose. We have now updated the connectomic analyses using an improved connectome dataset that was released during the revision of this manuscript. Our new analysis shows that lNSC^ITP are connected to other endocrine cells that produce other homeostatic hormones (new Figure 13F). We also identify a pathway through which other ITP-producing neurons (LNd^ITP) receive hygrosensory inputs to regulate water seeking behavior (new Figure 13E). Moreover, we now include results which showcase that ITPa-producing neurons (l-NSC^ITP) are active (new Figure 8A and B) and release ITPa under desiccation. Together with other analyses, these data provide a comprehensive outlook on the when, what and how ITPa regulates systemic homeostasis.  

Strengths:  

(1) The main strengths of this paper are i) the detailed analysis of the expression and actions of ITP and the phenotypic consequences of overexpression of ITPa in Drosophila. ii). the detailed analysis of the expression of Gyc76C and the phenotypic consequences of knockdown of Gyc76C expression in Drosophila.  

(2) Furthermore, the paper is generally well-written and the figures are of good quality. 

We thank this reviewer for highlighting the strengths of this manuscript.

Weaknesses:  

(1) The main weakness of this paper is that the data obtained do not prove that Gyc76C acts as a receptor for ITPa. Therefore, the following statement in the abstract is premature: "Using a phylogenetic-driven approach and the ex vivo secretion assay, we identified and functionally characterized Gyc76C, a membrane guanylate cyclase, as an elusive Drosophila ITPa receptor." Further experimental studies are needed to determine if Gyc76C acts as a receptor for ITPa. In the section of the paper headed "Limitations of the study", the authors recognise this weakness. They state "While our phylogenetic analysis, anatomical mapping, and ex vivo and in vivo functional studies all indicate that Gyc76C functions as an ITPa receptor in Drosophila, we were unable to verify that ITPa directly binds to Gyc76C. This was largely due to the lack of a robust and sensitive reporter system to monitor mGC activation." It is not clear what the authors mean by "the lack of a robust and sensitive reporter system to monitor mGC activation". The discovery of mGCs as receptors for ANP in mammals was dependent on the use of assays that measure GC activity in cells (e.g. by measuring cGMP levels in cells). Furthermore, more recently cGMP reporters have been developed. The use of such assays is needed here to investigate directly whether Gyc76C acts as a receptor for ITPa. In summary, insufficient evidence has been obtained to conclude that Gyc76C acts as a receptor for ITPa. Therefore, I think there are two ways forward, either:  

(a) The authors obtain additional biochemical evidence that ITPa is a ligand for Gyc76C.  

or  

(b) The authors substantially revise the conclusions of the paper (in the title, abstract, and throughout the paper) to state that Gyc76C MAY act as a receptor for ITPa, but that additional experiments are needed to prove this. 

We thank the reviewer for this comment and agree with the two options they propose. We had previously tried different a cGMP reporter (Promega GloSensor cGMP assay) to monitor activation of Gyc76C by ITPa in a heterologous system. Unfortunately, we were not successful in monitoring Gyc76C activation by ITPa. We now utilized another cGMP sensor, Green cGull, to show that ITPa can indeed activate Gyc76C heterologously expressed in HEK cells (new Figure 7 and Figure 7 Supplement 1). However, we still cannot rule out the possibility that ITPa can act on additional receptors in vivo. This is based on our ex vivo Malpighian tubule assays (new Figure 6E and F). ITPa inhibits DH31- and LK-stimulated secretion and we show that this effect is abolished in Gyc76C knockdown specifically in principal and stellate cells, respectively. Interestingly, application of ITPa alone can stimulate secretion when Gyc76C is knocked down in principal cells (new Figure 6E). This could be explained by: 1) presence of another receptor for ITPa which results in diuretic actions and/or 2) low Gyc76C signaling activity (RNAi based knockdown lowers signaling but does not abolish it completely) could alter other intracellular messenger pathways that promote secretion. We have added text to indicate the possibility of other ITPa receptors. Nonetheless, our conclusions are supported by the heterologous assay results which indicate that ITPa can activate Gyc76C. Therefore, we do not alter the title. 

(2) The authors state in the abstract that a phylogenetic-driven approach led to their identification of Gyc76C as a candidate receptor for ITPa. However, there are weaknesses in this claim. Firstly, because the hypothesis that Gyc76C may be involved in mediating effects of ITPa was first proposed ten years ago by Nagai et al. 2014, so this surely was the primary basis for investigating this protein. Nevertheless, investigating if there is correspondence in the phylogenetic distribution of ITP-type and Gyc76C-type genes/proteins is a valuable approach to addressing this issue. Unfortunately, the evidence presented is rather limited in scope. Essentially, the authors report that they only found ITP-type and Gyc76C-type genes/proteins in protostomes, but not in deuterostomes. What is needed is a more fine-grained analysis at the species level within the protostomes. Thus, are there protostome species in which both ITP-type and Gyc76C-type genes/proteins have been lost? Furthermore, are there any protostome species in which an ITP-type gene is present but an Gyc76C-type gene is absent, or vice versa? If there are protostome species in which an ITP-type gene is present but a Gyc76C-type gene is absent or vice versa, this would argue against Gyc76C being a receptor for ITPa. In this regard, it is noteworthy that in Figure 2A there are two ITP-type precursors in C. elegans, but there are no Gyc76Ctype proteins shown in the tree in Figure 2B. Thus, what is needed is a more detailed analysis of protostomes to investigate if there really is correspondence in the phylogenetic distribution of Gyc76C-type and ITP-type genes at the species level. 

We thank the reviewer for this comment. While the previous study by Nagai et al had implicated Gyc76C in the ITP signaling pathway, how they narrowed down Gyc76C as a candidate was not reported. Therefore, our unbiased phylogenetic approach was necessary to ensure that we identified all suitable candidate receptors. Indeed, our phylogenetic analysis also identified Gyc32E as another candidate ITP receptor. However, we did not pursue this receptor further as our expression data (new Figure 4 Supplement 2) indicated that Gyc32E is not expressed in osmoregulatory tissues and therefore likely does not mediate the osmotic effects of ITPa. 

We also appreciate the suggestion to perform a more detailed phylogenetic analysis for the peptide and receptor. We did not include C. elegans receptors in the phylogenetic analysis because they tend to be highly evolved and routinely cause long-branch attraction (see: Guerra and Zandawala 2024: https://doi.org/10.1093/gbe/evad108). We (specifically the senior author) have previously excluded C. elegans receptors in the phylogenetic analysis of GnRH and Corazonin receptors for similar reasons (see: Tian and Zandawala et al. 2016: 10.1038/srep28788). 

Unfortunately, absence of a gene in a genome is hard to prove especially when they are not as high-quality as the genomes of model systems (e.g. Drosophila and mice). Moreover, given the concern of this reviewer that our physiological and behavioral data on ITPa and Gyc76C only provide correlative evidence, we decided against performing additional phylogenetic analysis which also provides correlative evidence. Our only goal with this analysis was to identify a candidate ITPa receptor. Since we have now functionally characterized this receptor using a heterologous system, we feel that the current phylogenetic analysis was able to successfully serve its purpose.  

(3) The manuscript would benefit from a more comprehensive overview and discussion of published literature on Gyc76C in Drosophila, both as a basis for this study and for interpretation of the findings of this study.  

We thank the reviewer for this comment. We have now included a broader discussion of Gyc76C based on published literature.  

Reviewer #3 (Public Review):  

Summary:  

The goal of this paper is to characterize an anti-diuretic signaling system in insects using Drosophila melanogaster as a model. Specifically, the authors wished to characterize a role of ion transport peptide (ITP) and its isoforms in regulating diverse aspects of physiology and metabolism. The authors combined genetic and comparative genomic approaches with classical physiological techniques and biochemical assays to provide a comprehensive analysis of ITP and its role in regulating fluid balance and metabolic homeostasis in Drosophila. The authors further characterized a previously unrecognized role for Gyc76C as a receptor for ITPa, an amidated isoform of ITP, and in mediating the effects of ITPa on fluid balance and metabolism. The evidence presented in favor of this model is very strong as it combines multiple approaches and employs ideal controls. Taken together, these findings represent an important contribution to the field of insect neuropeptides and neurohormones and have strong relevance for other animals. 

We thank this reviewer for the positive and thorough assessment of our manuscript.

Strengths:  

Many approaches are used to support their model. Experiments were wellcontrolled, used appropriate statistical analyses, and were interpreted properly and without exaggeration.  

Weaknesses:  

No major weaknesses were identified by this reviewer. More evidence to support their model would be gained by using a loss-of-function approach with ITPa, and by providing more direct evidence that Gyc76C is the receptor that mediates the effects of ITPa on fat metabolism. However, these weaknesses do not detract from the overall quality of the evidence presented in this manuscript, which is very strong.  

We agree with this reviewer regarding the need to provide additional evidence using a loss-of-function approach with ITPa. We now characterize the phenotypes following knockdown of ITP in ITP-producing cells (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C. Unfortunately, we are not able to provide evidence that ITPa acts on Gyc76C in the fat body using the assay suggested by this reviewer (explained in detail below). Instead, we now provide direct evidence of Gyc76C activation by ITPa in a heterologous system (new Figure 7 and Figure 7 Supplement 1).

Reviewer #1 (Recommendations For The Authors):  

Here, I have several extra concerns about the work as below:  

(1) The authors confirmed the function of ITPa in regulating both osmotic and metabolic homeostasis by specifically overexpressing ITPa driven by ITP-RCGal4 in adult flies (Figures. 5 and 7). Have authors ever tried to knock down ITP in ITP-RC-Gal4 neurons? What was the phenotype? Especially regarding the impact on metabolic homeostasis, does knocking down ITP in ITP neurons mimic the phenotypes of Gyc76C fat body knockdown flies? 

We thank the reviewer for this suggestion. We now characterize the phenotypes following knockdown of ITP using ITP-RC-Gal4 (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C.

The authors mentioned that the existing ITP RNAi lines target all three isoforms. It would be interesting if the authors could overexpress ITPa in ITPRC-Gal4>ITP-RNAi flies and confirm whether any phenotypes induced by ITP knockdown could be rescued. It will further confirm the role of ITPa in homeostasis regulation.  

We thank the reviewer for this suggestion. Unfortunately, this experiment is not straightforward because knockdown with ITP RNAi does not completely abolish ITP expression (see Figure 9A). Hence, the rescue experiment needs to be ideally performed in an ITP mutant background. However, ITP mutation leads to developmental lethality (unpublished observation) so we cannot generate all the flies necessary for this experiment. Therefore, we cannot perform the rescue experiments at this time. In future studies, we hope to perform knockdown of specific ITP isoforms using the transgenes generated here (Xu et al 2023: 10.1038/s41586-023-06833-8).   

(2) In Figures 5A and B, the authors nicely show the increased release of ITPa under desiccation by quantifying the ITPa immunolabelling intensity in different neuronal populations. It may be induced by the increased neuronal activity of ITPa neurons under the desiccated condition. Have the authors confirmed whether the activity of ITPa-expressing neurons is impacted by desiccation?  

The TRIC system may be able to detect the different activity of those neurons before and after desiccation. This may further explain the reduced ITPa peptide levels during desiccation.  

We thank the reviewer for this suggestion. We have now monitored the activity of ITPa-expressing neurons using the CaLexA system (Masuyama et al 2012: 10.3109/01677063.2011.642910). Our results indicate that ITPa neurons are indeed active under desiccation (new Figure 8A and B). These results are also in agreement with ITPa immunolabelling showing increased peptide release during desiccation (new Figure 8C and D). Together, these results show that ITPa neurons are activated and release ITPa under desiccation.  

(3) What about the intensity of ITPa immunolabelling in other ITPa-positive neurons (e.g., VNC) under desiccation? If there is no change in other ITPa neurons, it will be a good control. 

We thank the reviewer for this suggestion. Unfortunately, ITPa immunostaining in VNC neurons is extremely weak preventing accurate quantification of ITPa levels under different conditions. We did hypothesize that ITPa immunolabelling in clock neurons (5^th-LN_v and LN<Sub>d</sub>^ITP) would not change depending on the osmotic state of the animal. However, our results (Figure 8C and D) indicate that ITPa from these neurons is also released under desiccation. Interestingly, LNd^ITP, which also coexpress Neuropeptide F (NPF) have recently been implicated in water seeking during thirst (Ramirez et al, 2025: 10.1101/2025.07.03.662850). Our new connectomic-driven analysis shows that these neurons can receive thermo/hygrosensory inputs (new Figure 13E). Hence, it is conceivable that other ITPa-expressing neurons also release ITPa during thirst/desiccation.

(4) The adult stage, specifically overexpression of ITPa in ITP neurons, does show significant phenotypes compared to controls in both osmotic and metabolic homeostasis-related assays. It would be helpful if authors could show how much ITPa mRNA levels are increased in the fly heads with ITPa overexpression (under desiccation & starvation or not). 

We thank the reviewer for this suggestion. We have now included immunohistochemical evidence showing increase in ITPa peptide levels in flies with ITPa overexpression (new Figure 10A). We feel that this is a better indicator of ITPa signaling level instead of ITPa mRNA levels.   

(5) Another question concerns the bloated abdomens of ITPa-overexpressing flies. Are the bloated abdomens of ITPa OE female flies (Figure 5E) due to increased ovary size (Figure 7G)? Have the authors also detected similar bloated abdomens in male flies with ITPa overexpression? Since both male and female flies show more release of ITPa during the desiccation.  

We thank the reviewer for this comment. The bloated abdomen phenotype seen in females can be attributed to increased water content since we see a similar phenotype in males (see Author response image 1 below).

Author response image 1.

Reviewer #2 (Recommendations For The Authors):  

(1) Page 1 - change "Homeostasis is obtained by" to "Homeostasis is achieved by".  

Changed

(2) Page 1 - change "Physiological responses" to "Physiological processes". 

Changed

(3) Page 2 - Change "Recently, ITPL2 was also shown to mediate anti-diuretic effects via the tachykinin receptor" to "Recently, ITPL2 was also shown to exert anti-diuretic effects via the tachykinin receptor". 

Changed

(4) Page 9 - "(C) Adult-specific overexpression of ITPa using ITP- RC-GAL4TS (ITP-RC-T2A-GAL4 combined with temperature-sensitive tubulinGAL80) increases desiccation" Unless I am misunderstanding Fig 5C, I think what is shown is that overexpression of ITPa prolongs survival during a period of desiccation. I am not sure what the authors mean by "increases desiccation". In the text (page 9) the authors state "ITPa overexpression improves desiccation tolerance, which is a much clearer statement than what is in the figure legend. 

We thank the reviewer for identifying this oversight. We have now changed the caption to “increases desiccation tolerance”.  

(5) Page 11 - The authors conclude that "increased ITPa signaling results in phenotypes that largely mirror those seen following Gyc76C knockdown in the fat body, providing further support that ITPa mediates its effects via Gyc76C." Use of the term "largely mirror" seems inappropriate here because there are opposing effects- e.g. decreased starvation resistance in Figure 6A versus increased starvation resistance in Figure 7A.  

Perhaps there is a misunderstanding of what is meant by "mirroring" - it means the same, not the opposite. 

We thank the reviewer for this comment. We agree that the use of the term “largely mirrors” to describe the effects of ITPa overexpression and Gyc76C knockdown is not appropriate and have changed this sentence as follows: “Taken together, the phenotypes seen following Gyc76C knockdown in the fat body largely mirror those seen following ITP knockdown in ITP-RC neurons, providing further support that ITPa mediates its effects via Gyc76C.”

(6) Page 12 - There appear to be words missing between "neurons during desiccation, as well as their downstream" and "the recently completed FlyWire adult brain connectome" 

We thank the reviewer for highlighting this mistake. We have changed the sentence as following: “Having characterized the functions of ITP signaling to the renal tubules and the fat body, we wanted to identify the factors and mechanisms regulating the activity of ITP neurons during desiccation, as well as their downstream neuronal pathways. To address this, we took advantage of the recently completed FlyWire adult brain connectome (Dorkenwald et al., 2024, Schlegel et al., 2024) to identify pre- and post-synaptic partners of ITP neurons.”

(7) Page 15 - "can release up to a staggering 8 neuropeptides" - I suggest that the word "staggering" is removed. The notion that individual neurons release many neuropeptides is now widely recognised (both in vertebrates and invertebrates) based on analysis of single-cell transcriptomic data. 

Removed staggering.

(8) Page 16 - "(Farwa and Jean-Paul, 2024)" - this citation needs to be added to the reference list and I think it needs to be changed to "Sajadi and Paluzzi, 2024". 

We thank the reviewer for highlighting this oversight. The correct citation has now been added.

(9) It is noteworthy that, based on a PubMed search, there are at least thirteen published papers that report on Gyc76C in Drosophila (PMIDs: 34988396, 32063902, 27642749, 26440503, 24284209, 23862019, 23213443,  21893139, 21350862, 16341244, 15485853, 15282266, 7706258). However, none of these papers are discussed/cited by the authors. This is surprising because the authors' hypothesis that Gyc76C acts as a receptor for ITPa surely needs to be evaluated and discussed with reference to all the published insights into the developmental/physiological roles of this protein. 

We thank the reviewer for this comment. Some of the references mentioned above (21350862, 16341244, 15485853) mainly report on soluble guanylyl cyclases and not membrane guanylyl cyclase like Gyc76C. Based on other studies on Gyc76C and its role in immunity and development, we have now expanded the discussion on additional roles of ITPa.

Reviewer #3 (Recommendations For The Authors):  

I have only a few comments that will help the authors strengthen a couple of aspects of their model.  

(1) The case for Gyc76C as a receptor for ITPa in regulating fluid homeostasis is clear, given the experiments the authors carried out where they applied ITPa to tubules and showed that the effects of ITPa on tubule secretion were blocked if Gyc76C was absent in tubules. This approach, or something similar, should be used to provide conclusive proof that ITPa's metabolic effects on the fat body go through Gyc76C.  

At present (unless I missed it) the authors only show that gain of ITPa has the opposite phenotype to fat body-specific loss of Gyc76C. While this would be the expected result if ITPa/Gyc76C is a ligand-receptor pair, it is not quite sufficient to conclusively demonstrate that Gyc76C is definitely the fat body receptor. Ex vivo experiments such as soaking the adult fat body carcasses with and without Gyc76C in ITPa and monitoring fat content via Nile Red could be one way to address this lack of direct evidence. The authors could also make text changes to explicitly mention this lack of conclusive evidence and suggest it as a future direction.

We thank the reviewer for this comment. We have now conclusively demonstrated that Gyc76C is activated by ITPa in a heterologous assay (new Figure 7 and Figure 7 Supplement 1). With this evidence, we can confidently claim that ITPa can mediate its actions via Gyc76C in various tissues including the Malpighian tubules and fat body. Nonetheless, we liked the suggestion by this reviewer to perform the ex vivo assay and test the effect of ITPa on the fat body. Unfortunately, it is challenging to do this because increased ITPa signaling (chronically using ITPa overexpression) results in increased lipid accumulation in the fat body in vivo. Therefore, we would likely not see the effect of ITPa addition in an ex vivo fat body preparation since lipogenesis will not occur in the absence of glucose. However, ITPa could counteract the effects of other lipolytic factors such as adipokinetic hormone (AKH). To test this hypothesis, we monitored fat content in the fat body incubated with and without AKH (see Author response image 2 below showing representative images from this experiment). Since we did not observe any differences in fat levels between these two conditions, we were unable to test the effects of ITPa on AKH-activity using this assay.

Author response image 2.

(2) I did not see any loss of function data for ITPa - is this possible? If so this would strengthen the case for a 1:1 relationship between loss of ligand and loss of receptor. Alternatively, the authors could suggest this as an important future direction. 

We agree with this reviewer regarding the need to provide additional evidence using a loss-of-function approach with ITPa. We have now characterized the phenotypes following knockdown of ITP in ITP-producing cells (new Figure 9). Our results are in agreement with phenotypes observed following Gyc76C knockdown, lending further support that ITPa mediates its effects via Gyc76C.

(3) For clarity, please include the sex of all animals in the figure legend. Even though the methods say 'females used unless otherwise indicated' it is still better for the reader to know within the figure legend what sex is displayed. 

We thank the reviewer for this suggestion and have now included sex of the animals in the figure legends.  

(4) Please state whether females are mated or not, as this is relevant for taste preferences and food intake. 

We apologize for this oversight. We used mated females for all experiments. This has now been included in the methods.  

(5) More discussion on the previous study on metabolic effects of ITP in this study compared with past studies would help readers appreciate any similarities and/or differences between this study and past work (Galikova 2018, 2022) 

We thank the reviewer for this suggestion. Unfortunately, it is difficult to directly compare our phenotypes with the metabolic effects of ITP reported in Galikova and Klepsatel 2022 because the previous study used a ubiquitous driver (Da-GAL4) to manipulate ITP levels. Ectopically overexpressing ITPa in non-ITP producing cells can result in non-physiological phenotypes. This is evident in their metabolic measurements where both global overexpression and knockdown of ITP results in reduced glycogen and fat levels, and starvation tolerance. Moreover, ITP-RC-GAL4 used in our study to overexpress and knockdown ITPa is more specific than the Da-GAL4 used previously. Da-GAL4 would include other ITP cells (e.g. ITP-RD producing cells). Since ITP is broadly expressed across the animal, it is difficult to parse out the phenotypes of ITPa and other isoforms using manipulations performed with Da-GAL4. We have mentioned this limitation in the results for ITP knockdown as follows: “A previous study employing ubiquitous ITP knockdown and overexpression suggests that Drosophila ITP also regulates feeding and metabolic homeostasis (Galikova and Klepsatel, 2022) in addition to osmotic homeostais (Galikova et al., 2018). However, given the nature of the genetic manipulations (ectopic ITPa overexpression and knockdown of ITP in all tissues) utilized in those studies, it is difficult to parse the effects of ITP signaling from ITPa-producing neurons.”

utilizing

Clue/Trail/Plex Mark Atomic Terms used for naming

info-morphic units of information that are high-resolution addressable high fildeilty meaning/intentfully deeply intertwingled named info-morphic-colab-orative interpersonal nterplanetary structures amenable to muassive multiplayer interplays that plays nicely with other structures

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Reply to the reviewers

Reviewer #1

Major comments:

(comment #1)- It is interesting that TRF2 loss not only fails to increase γH2AX/53BP1 levels but may even slightly reduce them (e.g., Fig. S2c and the IF images). While the main hypothesis is that TRF2 loss does not trigger telomere dysfunction in NSCs, this observation raises the possibility that TRF2 itself contributes to DDR signaling (ATM-P, γH2AX, 53BP1) in these cells and that in its absence, cells are not able to form those foci. To exclude the possibility that telomere-specific DDR is being missed due to an overall dampened DDR response in the absence of TRF2, it would be informative to induce exogenous DSBs in TRF2-depleted cells and test DDR competence (e.g., IF for γH2AX/53BP1). In other words, are those NSC lacking TRF2 even able to form H2AX/53BP1 foci when damaged? In addition, it would be interesting to perform telomere fusion analysis in TRF2 silenced cells (and TRF1 silenced cells as a positive control).

We acknowledge a slight reduction; however, this difference is not statistically significant (Fig S2c,e). We will quantify the levels of DDR markers upon TRF2 loss and exogenous DSBs and include it in the subsequent revision.

(comment #2)-A TRF2 ChIP-seq should be performed in NSC as this list of genes (named TAN genes in the text) was determined using a ChIP performed in another cell line (HT1080). For the ChIP-qPCR in the various conditions, primers for negative control regions should be included to show the specific binding of TRF2 to the promoter of the genes associated with neuronal differentiation. For example, an intergenic region and/or promoters of genes that are not associated with neuronal differentiation (or don't contain a potential G4). The same comment goes true for the gene expression analysis: a few genes that are not bound by TRF2 should be included as negative controls to exclude a potential global effect of TRF2 loss on gene expression (ideally a RNA-seq would be performed instead). We have performed NSC-specific TRF2 ChIP-seq for an upcoming manuscript, which confirms TRF2 occupancy at multiple promoters of differentiation-associated genes. These data are provided solely for confidential evaluation by the designated reviewers.

Regarding the ChIP-qPCR control experiments: We thank reviewer for pointing this out, indeed we included controls in our PCR assays as positive (telomeric) and TRF2-nonbinding loci (GAPDH, RPS18, and ACTB, based on HT1080 TRF2 ChIP-seq data) as negative controls. These results were not included earlier for clarity given that we were presenting several ChIP-PCR figures - in response to the comment we have included this now in the revised version (Fig. S3d,e). Gene expression analyses show selective upregulation of the TAN genes upon TRF2 loss (data normalised to GAPDH); whereas negative control genes lacking TRF2 binding (RPS18, ACTB) remain unchanged, ruling out non-specific effects. (Fig S3f,g,j,k).

-(comment #3) A co-IP should be performed between the TRF2 PTM mutant K176R or WT TRF2 and REST and PRC2 components to directly show a defect of interaction between them when TRF2 is mutated (a co-IP with DNase/RNase treatment to exclude nucleic-acid bridging). The TRF2 PTM mutant T188N also seems to lead to an increased differentiation (Fig. S5a). Could the author repeat the measure of gene expression and co-IP with REST upon the overexpression of this mutant too?

We confirm that DNase/RNase is routinely included in our pull-down experiments to exclude nucleic-acid bridging, with detailed methodology now elaborated in the Methods section. Not including this in the manuscript Methods was an oversight from our side. Our data demonstrate that only REST directly interacts with TRF2, while TRF2 engages PRC2 indirectly via REST, as also previously shown by us and others (page 6; ref. [62]; Sharma et al., ref. [15]).

We thank the reviewer for noting the apparent differentiation in Fig. S5a. However, this observation represents rare spontaneous differentiation event and is not statistically significant (as shown in Fig S5b). Consistently, gene expression analysis of the TRF2-T188N mutant shows no significant change in TRF2-associated neuronal differentiation (TAN) genes. Therefore, Co-IP for TRF2-T188N with REST was not done.

(comment #4) - The authors show that the G4 ligands SMH14.6 and Bis-indole carboxamide upregulate TAN genes and promote neuronal differentiation, but the underlying mechanism remains unclear. Bis-indole carboxamide is generally considered a G4 stabilizer, while SMH14.6 is less characterized and should be better introduced. The authors should clarify how G4 stabilization would interfere with TRF2 binding, it seems that it would likely be by blocking access. A more detailed discussion, and ideally TRF2 ChIP after ligand treatment and/or G4 helicase treatment, would strengthen the model.

We clarify that Bis-indole carboxamide acts as a G4 stabilizer, while SMH14.6 is also a noted G4-binding ligand that stabilizes G4s (ref. [15]). The exclusion of TRF2 from G4 motifs in gene promoters by G4-binding ligands has also been documented previously (ref. [18]). In line with these findings, ChIP experiments performed following ligand treatment revealed a decreased occupancy of TRF2 at TAN gene promoters, supporting the proposed mechanism (added Fig. 6h).

Minor comments:

• Supp Figures related to the scRNA-seq are difficult to read (blurry).

Corrected

• Fig S1h: The red box mentioned in the legend is not visible

Corrected

• In the text, the Figures 1 f-g are misannotated as Fig 1m and l

Corrected

• The symbol γ of γH2AX is missing in the text

Corrected

• Fig.3d, please indicate in the legend that it is done in SH-SY5Y.

Added SH-SY5Y in the legend of Fig. 3d.

• Fig. S3b: Please consider replotting this panel with an increased y-axis scale. As currently presented, the TRF2 ChIP-seq peaks at several promoters appear truncated by the scaling.

Corrected

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

1. For most of the data graphs in the manuscript, there is no indication of the number of independent biological replicates carried out (which should ideally be plotted as individual dots overlaying the column graphs), or what the error bars represent, or what statistical test was used. All the figure legends and methods have now been updated with the corresponding biological replicates per experiment, with error bars as SD/SEM and the corresponding statistical test along with p values.

Figure S1.1a: needs a marker to show that the tissue is dentate gyrus.

We acknowledge the reviewers' concern that high-magnification images alone make it difficult to verify whether the fields are taken from the correct anatomical location. The dentate gyrus (DG) of the hippocampus is a well-defined structure. In the revised figure (Fig S1.1a), we now include a low-magnification image showing the entire hippocampus, including the CA fields, along with two high-magnification fields specifically from the DG region. Consistent with our claim, the co-immunostaining demonstrates that Sox2-positive neural stem cells in the DG are also positive for TRF2.

Figure 1c (and all other flow cytometry panels throughout the manuscript): it is not clear if the expression of any of these proteins, except maybe MAP2, are significantly different in the presence or absence of TRF2. These differences need to be presented more quantitatively, with the results compiled from multiple biological replicates and analysed statistically. I am not sure that flow cytometry is the best way to determine differences in protein expression levels for non-surface proteins, because many of the reported differences are not at all convincing.

To detect intracellular/nuclear proteins by flow cytometry, cells were permeabilized using pre-chilled 0.2% Triton X-100 for 10 minutes, as described in the Methods section.

We have revised the figures (Fig 1c,e) and now included statistical analysis from three independent biological replicates for these experiments.(Fig S1.4h-j, S2e, S6d)

Fig 1d: has TRF2 been effectively silenced in this experiment? There appears to be just as many TRF2+ nuclei in the "TRF2 silenced" panel vs the control, including in the cells with neurite outgrowths.

Quantification of nuclear levels of TRF2 showing decrease in nuclear TRF2 has been included in supplementary Fig S1g.

Fig 2a-c: these experiments need a positive control, showing increased expression of these proteins in mNSC and SH-SY5Y cells in response to a DNA damaging agent. Again, flow cytometry may not be the best method for this; immunofluorescence combined with telomere FISH would be more convincing.

We confirm that doxorubicin induces 53BP1 foci (IF-FISH Sup Fig. S2b) and TRF1 silencing elevates γH2AX (Sup Fig. S2c) validating DDR sensitivity. Unlike TRF2 loss (Fig. 2a-c), no TIFs appear with IF and telomere probes (Fig. 2d, Sup Fig. 2a), and without TIFs, there is no telomeric fusion. Flow cytometry was performed with Triton X- 100 to target nuclear protein. These findings adequately address the concern; therefore, further IF-FISH experiments were not included in the present study.

To conclude that telomere damage is not occurring, an independent marker of such damage, such as telomere fusions, should also be measured.

In response to uncapped telomeres, ATM kinase activates the DNA damage response (DDR), recruiting γH2AX and 53BP1 to telomeres, which precedes the end-to-end fusions (Takai et al., 2003; Maciejowski & de Lange, 2015; Takai et al., 2003; d'Adda di Fagagna et al., 2003; Cesare & Reddel, 2010; Hayashi et al., 2012; Sarek et al., 2015). We observe no DDR activation or foci (Fig. 2; Sup. Fig. 2). This absence of a DDR response and TIFs indicates no telomere uncapping, negating the need for direct telomere fusion analysis.

Figure S2b is lacking a no-doxorubicin control.

Untreated control has been included Fig. S2b.

Figures 3a and 3b need a positive control (e.g. TRF2 binding to telomeric DNA) and a negative control (e.g. a promoter that did not show any TRF2 binding in the HT1080 ChiP-seq experiment in Fig S3).

We have included positive (telomere) and negative (GAPDH) controls (based on HT1080 TRF2 ChIP-seq data) for the TRF2 ChIP assay in Supplementary Fig. S3d,e. Additionally, positive and negative controls for all ChIP experiments conducted in this study are presented in Supplementary Figs. S3d, S3e, S3h, S3i, S4c-h, and S5c-e

The data in Figure 3 would be more compelling if all experiments were also performed in fibroblasts to confirm the cell-type specificity of the effect.

Our HT1080 fibrosarcoma ChIP-seq data (ref. [18]; Sup. Fig. 3a,b) show TRF2 binding to TAN gene promoters in a fibroblast-derived model, with enrichment in neurogenesis-related genes (refs. [19,20]). In fibroblasts TRF2 depletion, as expected, induce telomere dysfunction and DDR (Fig. 2d; Sup. Fig. 2a), and eventually cell-cycle arrest and cell death as also reported earlier (van Steensel et al., 1998; Smogorzewska & de Lange, 2002). Therefore, the suggested experiments which would require sustained TRF2-depletion are not possible to perform in fibroblasts. TRF2 occupancy on the promoter of the genes in question in cells other than NSC was noted in HT1080 cells (ref. [18]; Sup. Fig. 3a,b).

No references are provided for the TRF2 posttranslational modifications on R17, K176, K190 and T188. What is the evidence for these modifications, and is it known if they participate in the telomeric role of TRF2?

These lines with references have been included in the manuscript (highlighted in blue).

R17 methylation enhances telomere stability (66). K176/K190 acetylation stabilizes telomeres and is deacetylated by SIRT6 (67). T188 phosphorylation facilitates telomere repair after DSBs(68). These PTMs primarily support telomeric roles.

The experiments in Fig 5 should also be performed with WT TRF2, to confirm that effects are not due to the overexpression of TRF2.

WT TRF2 shows no differentiation phenotype and change in TAN gene expression (Fig. 1f,g; 3h, Sup Fig. 5a). Confirming effects are not due to TRF2 overexpression.

Fig 5c has not been described in the text, and there are multiple technical problems with the TRF2 WT experiment: i) There appears to be significant background binding of REST to the IgG beads, though this blot has such high background it is hard to tell (the REST blot in Fig S4b is also of poor quality), ii) TRF2 is migrating at two different positions in the Input and IP lanes, and the TRF2 band in the K176R blot is at a different position to either, and iii) the relative loading of the Input and IP lanes is not indicated, so it's not clear why K176R appears to be so enriched in the IP.

We acknowledge the oversight in not citing Fig 5c in the manuscript. This has been corrected, and, highlighted in blue in the revised manuscript.

i) Multiple optimization attempts were made for the Co-IP experiments, and the presented figure reflects the best achievable result despite REST blot smearing, a pattern also reported previously (Ref. 65). The TRF2-REST interaction is well established, and a similar background was also observed in the cited study

ii)Variable migration patterns of TRF2 were also noted in the cited study (Ref. 65), consistent with our observations. Our primary emphasis, however, is on the TRF2 K176R mutant, which clearly disrupts its interaction with REST.

iii)The input loading corresponds to 10% of the total lysate. As the experiments were conducted independently, variations in transfection and pull-down efficiencies may account for observed differences.

To rule out indirect effects of the G4 ligands on the results in Fig 6g, the binding of BG4 and TRF2 at the promoters of these genes should be measured by ChIP.

To confirm that G4 ligand effects on TAN gene promoters are direct, TRF2 occupancy was assessed using ChIP. Significantly decreased occupancy of TRF2 was noted at TAN gene promoters, (added Fig. 6h). This implies that ligand-induced changes in TRF2 binding are directly linked to promoter-level G4 stabilization.

Minor comments:

1. The size of all the size markers in western blots should be added to the figures. Size has been included in all the western blots

2. There are several figure panels that are incorrectly referenced in the text, e.g. Fig S1.1 (e-f) should be Fig S1.1 (e-h); Fig. 1m should be Fig. 1f; Figs 5e and 5f have been swapped.

Corrected.

1. Fig S1.4 is not referred to in the text. It is not clear what the purpose of Fig S1.4a is.

The following line has been included in the manuscript highlighted in blue.

Neurospheres were characterized using PAX6, a NSC marker (Fig S1.4a).

Are the experiments in Figs 3e, 4a, 4c and 4e using 4-OHT treatment, or siRNA? If the latter, I don't think a control for the effectiveness of the knockdown in this cell type has been included anywhere in the manuscript.

It is using siRNA, a western blot showing the effectiveness of knockdown is presented in supplementary figure S4c (now S4a).

The lanes of the western blots in Fig S4c are not labelled.

Corrected.

1. Given that the experiments in Fig 5 were carried out on a background of endogenous WT TRF2 expression, presumably the K176R mutant is having a dominant negative effect. To understand the mechanism of this effect (e.g, is it simply due to replacement of endogenous WT TRF2 at its genomic binding sites by a large excess of exogenous K176R, or is dimerisation with WT TRF2 needed?) it would be helpful to know the relative expression levels of endogenous and K176R TRF2.

To address the query, qRT-PCR with 3′ UTR-specific primers showed no change in endogenous TRF2 mRNA upon K176R expression in SH-SY5Y cells, while primers detecting total TRF2 revealed ~10-fold higher expression of K176R compared to control (Figure below). This indicates the absence of suppression of endogenous TRF2 mRNA. Given that the mutant's DNA binding is intact (Fig. 5f), the dominant-negative effect of K176R likely arises from overexpression of the exogenous mutant.

For the sentence "...and critical for transcription factor binding including epigenetic functions that are G4 dependent" (bottom of page 3 of the PDF), the authors cite only their own prior papers, but there are examples from others that could be cited.

We have incorporated citations from other research groups, now included as references 23-26.

Author response:

Reviewer #1:

We agree with the reviewer that a limitation of our study is its focus on cell-based assays rather than in vivo experiments. We did consider evaluating the effects of statins on B cell responses in vivo; however, this approach is complicated by findings that statins can influence antigen presentation by dendritic cells, thereby impacting antibody responses (Xia et al, 2018). One possible solution would be to use B cell-specific conditional knockout models to study the roles of the identified proteins in an in vivo context. However, we currently do not have access to these models and were therefore unable to include such experiments within a feasible timeframe. We will revise the discussion section to acknowledge these points.

The reviewer also noted that our study assessed the roles of HMGCR, SQLE, and prenylation in B cell activation using pharmacological inhibitors and genetic knockdown/out approaches. Loss-of-function techniques such as RNAi, siRNA, and CRISPR can be challenging to apply to primary B cells, but we are exploring their feasibility for future revisions. While we acknowledge the limitations of using pharmacological inhibitors, we have taken several steps to mitigate these, including targeting multiple steps in the cholesterol biosynthetic pathway using structurally distinct inhibitors and conducting rescue experiments by supplementing downstream metabolites. To further investigate potential off-target effects of statins, we have recently performed proteomic analysis of B cells treated with and without fluvastatin. The data suggest that fluvastatin primarily affects cholesterol metabolism and does not cause widespread off-target effects. We will include this new data in the revised manuscript.

Reviewer #2:

The reviewer suggested that the study would be strengthened by determining whether the observed changes are specific to LPS + IL-4 stimulation or represent a more general B cell response to mitogenic signals.

A complementary study by James et al. (James et al, 2024) investigated murine B cells stimulated via the B cell receptor (BCR) and CD40, using anti-IgM and anti-CD40 antibodies alongside IL-4. Their proteomic analysis showed that such co-stimulation induces a fivefold increase in total cellular protein mass within 24 hours, mirroring our findings with LPS + IL-4. They also reported upregulation of proteins associated with cell cycle progression, ribosome biogenesis, and amino acid transport. Furthermore, by using SLC7A5 knockout mice, they demonstrated that this transporter is required for B cell activation. We will expand our discussion to include and these findings.  We will also expand on the final figure in our paper showing that the effects of statins are not limited to LPS.

References:

James O, Sinclair LV, Lefter N, Salerno F, Brenes A & Howden AJM (2024) A proteomic map of B cell activation and its shaping by mTORC1, MYC and iron. bioRxiv 2024.12.19.629506 doi:10.1101/2024.12.19.629506 [PREPRINT]

Xia Y, Xie Y, Yu Z, Xiao H, Jiang G, Zhou X, Yang Y, Li X, Zhao M, Li L, et al (2018) The Mevalonate Pathway Is a Druggable Target for Vaccine Adjuvant Discovery. Cell 175: 1059-1073.e21

Author response:

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

Reviewer #1 (Public review):

(1) The authors should provide a detailed description of the pathogenesis of Haemorrhagic Fever with Renal Syndrome (HFRS) and elaborate on the crucial role of IgG proteins in the disease's progression (line 65).

As suggested, we have now provided a detailed description of the pathogenesis of HFRS and elaborated on the crucial role of IgG proteins in the disease's progression:

"Hantaviruses are tri-segmented, single-stranded, negative-sense RNA viruses, whose genomes consist of three regions: large (L), medium (M), and small (S). The glycoproteins Gn and Gc, encoded by the M segment, can infect target cells - primarily vascular endothelial cells - via β3 integrin receptors (Pizarro et al., 2019). Simultaneously, they could also infect other cell types, such as mononuclear macrophages and dendritic cells, leading to systemic viral infection. Although hantavirus replication is thought to occur primarily in the vascular endothelium without direct cytopathic effects, a plethora of innate immune cells mediate host antiviral defenses. These include natural killer cells, neutrophils, monocytes, and macrophages, together with pattern recognition receptors (PRRs), interferons (IFNs), antiviral proteins, and complement activation, e.g., via the pentraxin 3 (PTX3) pathway, which can exacerbate HFRS disease progression leading to immunopathological damage through cytokine/chemokine production, cytoskeletal rearrangements in endothelial cells, ultimately amplifying vascular dysfunction (Tariq & Kim, 2022). Rapid and effective humoral immune responses, however, such as neutralizing antibody responses targeting the glycoproteins Gn/Gc, contribute to rapid recovery from HFRS and are critical for protection from severe disease (Engdahl & Crowe, 2020; Li et al., 2020)." Please see the Introduction (Page 4, lines 65-81).

(2) An additional discussion on the significance of glycosylation, particularly IgG N-glycosylation, in viral infections should be included in the Introduction section.

Thank you for the suggestion and we have added an additional discussion on the significance of glycosylation in viral infections in the revised Introduction section.

"Immunoglobulin G (IgG) N-linked glycosylation mediates critical functions modulating antiviral immunity during viral infection. Changes in the conserved N-linked glycan Asn297 in the Fc region of IgG typically by fucosylation, galactosylation, or sialylation can alter antibody effector function. A reduction in core fucosylation decreases IgG binding to NK cell FcγRIIIa promotes antibody-dependent cellular cytotoxicity (ADCC) necessary for clearance of viruses, including SARS-CoV-2, dengue and HIV-1 whereas sialylation can attenuate immune responses resulting in immune evasion (Ash et al., 2022; Haslund-Gourley et al., 2024; Hou et al., 2021; Wang et al., 2017). Changes in IgG and other protein N-linked glycosylation profiles therefore shape virus-host interactions and disease progression." (Page 4, lines 82-91).

(3) In the abstract section, the authors state that HTNV-specific IgG antibody titers were detected and IgG N-glycosylation was analyzed. However, the analysis of plasma IgG N-glycans is described in the Methods section. Therefore, the authors should clarify the glycome analysis process. Was the specific IgG glycome profile similar to the total IgG N-glycome? Given the biological relevance of specific IgG in immunological diseases, characterizing the specific IgG N-glycome profile would be more significant than analyzing the total plasma IgG.

We are grateful to the reviewer for the comments. Previous studies on viral infections have revealed that the pattern of virus-specific IgG N-glycans may be similar to that of total IgG N-glycome, and we therefore analyzed the total plasma IgG glycosylation profiling in the HFRS patients. However, we have discussed this in the Discussion section.

"Despite establishing a well-characterized patient cohort and performing systematic IgG glycosylation profiling based on HTNV NP antibody status, this study has several noteworthy limitations. Most notably, while preliminary comparisons suggested similar patterns between virus-specific and total IgG N-glycome, our total plasma IgG analysis may have introduced confounding factors in the observed associations. This methodological constraint could potentially affect the interpretation of certain disease-specific glycosylation signatures." Please see the Discussion (Page 12, lines 274-280). 

References

(1) Mads Delbo Larsen, Erik L de Graaf, Myrthe E Sonneveld, et al. Afucosylated IgG characterizes enveloped viral responses and correlates with COVID-19 severity. Science . 2021 Feb 26;371(6532):eabc8378.

(2) Chakraborty S, Gonzalez J, Edwards K, et al. Proinflammatory IgG Fc structures in patients with severe COVID-19. Nat Immunol. 2021 Jan;22(1):67-73.

(3) Tea Petrović, Amrita Vijay, Frano Vučković, et al. IgG N-glycome changes during the course of severe COVID-19: An observational study. EBioMedicine. 2022 Jul ;81: 104101. 

(4) Hou H, Yang H, Liu P, et al. Profile of Immunoglobulin G N-Glycome in COVID-19 Patients: A Case-Control Study. Front Immunol. 2021 Sep 23;12:748566.

(4) Further details regarding the N-glycome analysis should be provided, including the quantity of IgG protein used and the methodology employed for analyzing IgG N-glycans (lines 286-287).

As suggested, we have provided further details regarding the N-glycome analysis in the Method section.

"Briefly, the diluted plasma samples were transferred onto a 96-well protein G monolithic plate (BIA Separations, Slovenia) for the isolation of IgG. The isolated IgG was eluted with 1 mL of 0.1 M formic acid and was immediately neutralized with 170 µL of 1M ammonium bicarbonate.

The released N-glycans were labelled with 2-aminobenzamide (2-AB) and were then purified from a mixture of 100% acetonitrile and ultrapure water in a 1:1 ratio (v/v). This was then analyzed by hydrophilic interaction liquid chromatography using ultra-performance liquid chromatography (HILIC-UPLC; Walters Corporation, Milford, MA) (Hou et al., 2019). As previously reported, the chromatograms were separated into 24 IgG glycan peaks (GPs) (Menni et al., 2018)." Please see the Method section (Page 15, lines 346-355).

(5) Additional statistical analyses should be performed, including multiple comparisons with p-value adjustment, false discovery rate (FDR) control, and Pearson correlation (line 291).

As suggested, we have performed additional statistical analyses and mentioned the results in the revised manuscript.

"Positive correlations were observed between the ASM subsets and both galactosylation (p=0.017, r_s=0.418) and sialylation (p=0.008, r_s=0.458) in the antibody Fc region, as well as between the PB subsets and sialylation (p=0.036, r_s=0.372) (Figure 4A-C). (Page 8, lines 180-183)"

"The Benjamini - Hochberg (BH) method was used to adjust the raw p-values from DEG analysis, controlling the false discovery rate (FDR)." Please see the Materials and Methods (Page 16, lines 369-371).

(6) Quality control should be conducted prior to the IgG N-glycome analysis. Additionally, both biological and technical replicates are essential to assess the reproducibility and robustness of the methods.

Thank you for the suggestion. We have added descriptions on the biological and technical replicates in the Method section.

"Our study incorporated both biological and technical replicates to ensure a robust glycomic profiling analysis. Specifically, we analyzed paired acute/convalescent-phase samples from 65 confirmed HFRS patients to assess inter-individual biological variability, while technical reproducibility was validated through comparison with standard chromatographic peak plots (Vučković et al., 2016). This dual-replicate strategy enabled a comprehensive evaluation of both biological heterogeneity and assay precision." (Page 15, lines 356-362).

(7) Multiple regression analysis should be conducted to evaluate the influence of genetic and environmental factors on the IgG N-glycome.

As suggested, we have conducted multiple regression analysis to evaluate the influence of genetic and environmental factors on the IgG N-glycome. These results have been provided in the revised Result section.

"Multivariate linear regression was employed to mitigate potential confounding by genetic and environmental factors in the glycomics analysis. While no significant associations were observed for most glycan models (fucosylation, p=0.526; bisecting GlcNAc, p=0.069; and sialylation, p=0.058), we discovered sex showed a potentially influential effect on galactosylation (p=0.001) (Supplementary files 5-8). These results suggest that while most glycan features appear unaffected by the examined covariates, galactosylation may be subject to sex-specific biological regulation." (Page 7, lines 153-160).

(8) Line 196. Additional discussions should be included, focusing on the underlying correlation between the differential expression of B-cell glycogenes and the dysregulated IgG N-glycome profile, as well as the potential molecular mechanisms of IgG N-glycosylation in the development of HFRS.

Thank you for your suggestions. We have added these contents in the Discussion section.

"Antibody-related glycogenes are significantly activated following Hantaan virus infection. We noted that ribophorin I and II (RPN1 and RPN2) were significantly upregulated in the ASM/IM/PB/RM subsets after Hantaan virus infection, which linked the high mannose oligosaccharides with asparagine residues found in the Asn-X-Ser/Thr consensus motif (Hwang et al., 2025). We speculate that they continuously attach the synthesized glycan chains to the constant region of antibodies during antibody synthesis. Similarly, fucosyltransferase 8 (FUT8) in the ASM subset, catalyzing the alpha1-2, alpha1-3, and alpha1-4 fucose addition (Wang & Ravetch, 2019; Yang et al., 2015), was downregulated in the mRNA translation, and the levels of fucosylated antibodies were naturally lower in the acute HFRS patients. Meanwhile, the beta-1,4-galactosyltransferase (beta4GalT) gene expression was significantly elevated in the ASM subpopulation during the acute phase, which also correlated with increased levels of galactosylated antibodies in serum (Wang & Ravetch, 2019). However, we did not observe significant upward changes in sialyltransferase mRNA expression in the acute HFRS patients, similar with the finding from severe COVID-19 cohorts (Haslund-Gourley et al., 2024). The neuraminidase 1 (NEU1) gene is strikingly upregulated and may potentially explain the decreased sialylation on the secreted HTNV-specific IgG antibodies during convalescence. Overall, the glycosylation of immunoglobulin G is regulated by a large network of B-cell glycogenes during HTNV infection." Please see the Discussion (Page 11, lines 254-273).

Reviewer #2 (Public review):

(1) While it is great to reference prior publications in the Materials and Methods section, the current level of detail is insufficient to clearly understand the study design and experimental procedures performed. Readers should not be expected to consult multiple previous papers to grasp the core methodological aspects of the present paper. For instance, the categorization of HFRS patients into different clinical subtypes/ courses, and the methods for measuring Fc glycosylation should be explicitly described in the Materials and Methods section of this manuscript. 

Many thanks for your comments. We have added more details regarding the study design and experimental procedures in the Materials and Methods section. "Clinical specimens were collected from HFRS patients who were hospitalized in Baoji Central Hospital between October 2019 and January 2022. Patients were categorized into four clinical subtypes (mild, moderate, severe, and critical) based on the diagnostic criteria for HFRS issued by the Ministry of Health (Ma et al., 2015). This study was approved by the ethics committee of the Shandong First Medical University & Shandong Academy of Medical Sciences (R201937). Written informed consent was obtained from each participant or their guardians.

The clinical course of HFRS is grouped into acute (febrile, hypotensive, and oliguric stages) and convalescent (diuretic and convalescent stages) phases. The acute phase was defined as within 12 days of illness onset, and the convalescent phase was defined as a period of illness lasting 13 days or longer (Tang et al., 2019; Zhang et al., 2022). The earliest sample was selected if there were multiple blood samples available in the acute phase and the last available sample before discharge was selected if there were multiple blood samples in the convalescent phase.

Briefly, the diluted plasma samples were transferred onto a 96-well protein G monolithic plate (BIA Separations, Slovenia) for the isolation of IgG. The isolated IgG was eluted with 1 mL of 0.1 M formic acid and was immediately neutralized with 170 µL of 1M ammonium bicarbonate.

The released N-glycans were labelled with 2-aminobenzamide (2-AB) and were then purified from a mixture of 100% acetonitrile and ultrapure water in a 1:1 ratio (v/v). This was then analyzed by hydrophilic interaction liquid chromatography using ultra-performance liquid chromatography (HILIC-UPLC; Walters Corporation, Milford, MA) (Hou et al., 2019). As previously reported, the chromatograms were separated into 24 IgG glycan peaks (GPs) (Menni et al., 2018)." Please see the Materials and Methods (Page 13, lines 290-303, and Page 15, lines 346-355).

(2) The authors should explain the nature of their cohort in a bit more detail. While it appears that HFRS cases were identified based on IgM ELISA and/or PCR, these are indicators of the Haantan virus infection. My understanding is that not all Haantan virus infections progress to HFRS. Thus, it is unclear whether all patients in the HFRS group actually had hemorrhagic fever. This distinction is critical for interpreting how the results observed relate to disease severity.

We are sincerely grateful for this valuable suggestion. We have carefully revised Figure 1 and the texts (Page 5, lines 104-107) in the revised manuscript.

"To characterize the humoral immune profiles in HFRS patients, we enrolled 166 suspected HTNV-infected patients who were admitted to Baoji Central Hospital in Shaanxi Province, China, between October 2019 and January 2022. Among them, 65 met the inclusion criteria and were included in the study (Figure 1)."

(3) The authors state that: "A 4-fold or greater increase in HTNV-NP-specific antibody titers usually indicates a protective humoral immune response during the acute phase", but they do not cite any references or provide any context that supports this claim. Given that in their own words, one of the most significant findings in the study is changes in glycosylation coinciding with this 4-fold increase, it is important to ground this claim in evidence. Without this, the use of a 4-fold threshold appears arbitrary and weakens the rationale for using this immune state as a proxy for protective immunity.

Thank you for the suggestion and we have provided relevant references in the Results section (Page 8, lines 171-173).

According to the Expert Consensus on Prevention and Treatment of Hemorrhagic  Fever with Renal Syndrome (HFRS) (https://ts-cms.jundaodsj.com/file/163823638693909.pdf), a confirmed diagnosis requires, based on a suspected or clinical diagnosis, one of the following: positive serum-specific IgM antibodies, detection of Hantavirus RNA in patient specimens, a four-fold or greater rise in titer of serum-specific IgG antibodies in the convalescent phase compared to the acute phase, or isolation of Hantavirus from patient specimens. A four-fold or greater rise in titer of convalescent serum-specific IgG antibodies compared to the acute phase not only suggests a recent Hantaan virus infection, but also the production of antibodies helping to combat the viral infection. In addition, the antibody glycosylation modifications may thus play a significant role in the antiviral immune response.

(4) The authors also claim that changes in Fc glycosylation influence recovery from HFRS - a point even emphasized in the manuscript title. However, this conclusion is not well supported by the data for two main reasons. First, the authors appear to measure bulk IgG Fc glycans, not Fc glycans of Hantaan virus-specific antibodies. While reasonable, this is something that should be communicated in the manuscript. Hantaan virus-specific antibodies are likely a very small fraction of total circulating IgG antibodies (perhaps ~1%), even during acute infection. As a result, changes in bulk Fc glycosylation may (or may not) accurately reflect the glycosylation state of Hantaan virus-specific antibodies. Second, even if the bulk Fc glycan shifts do mirror those of Hantaan virus-specific antibodies, it remains unclear whether these changes causally drive recovery or are merely a consequence of the infection being resolved. Thus, while the differences in Fc glycosylation observed are interesting - and it is tempting to speculate on their functional significance - the manuscript treats the observed correlations as causal mechanistic insight without sufficient data or justification.

Thank you for your valuable comments. This study measured bulk IgG Fc glycans, not Fc glycans of Hantaan virus-specific antibodies. We have described this limitation in the Discussion section (Page 12, lines 274-280). As reported in previous studies (references provided below), the changed pattern of virus-specific IgG N-glycans may reflect the total IgG N-glycome. Nevertheless, more studies are clearly needed to directly measure virus-specific IgGs and to clarify the causal mechanistic insights.

References

(1) Mads Delbo Larsen, Erik L de Graaf, Myrthe E Sonneveld, et al. Afucosylated IgG characterizes enveloped viral responses and correlates with COVID-19 severity. Science. 2021 Feb 26;371(6532): eabc8378.

(2) Chakraborty S, Gonzalez J, Edwards K, et al. Proinflammatory IgG Fc structures in patients with severe COVID-19. Nat Immunol. 2021 Jan;22(1):67-73.

(3) Tea Petrović, Amrita Vijay, Frano Vučković, et al. IgG N-glycome changes during the course of severe COVID-19: An observational study. EBioMedicine. 2022 Jul ;81: 104101. 

(4) Hou H, Yang H, Liu P, et al. Profile of Immunoglobulin G N-Glycome in COVID-19 Patients: A Case-Control Study. Front Immunol. 2021 Sep 23;12: 748566.

(5) Fc glycosylation is known to be influenced by covariates such as age and sex. While it is helpful that the authors stratified the patients by age group and looked for significant differences in glycosylation across them, a more robust approach would be to directly control for these covariates in the statistical analysis - such as by using a linear mixed effects model, in which disease state (e.g., acute vs. convalescent), age, and sex are treated as fixed effects, and subject ID is included as a random effect to account for repeated measures. This would allow the authors to assess whether observed differences in Fc glycosylation remain significant after accounting for potential confounders. This could be important given that some of the reported differences are quite small, for example, 94.29% vs. 94.89% fucosylation.

Thank you for your valuable suggestion. As suggested, we have conducted multiple regression analysis to evaluate the influence of genetic and environmental factors on the IgG N-glycome, and have provided these results in the revised Result section.

"Multivariate linear regression was employed to mitigate potential confounding by genetic and environmental factors in the glycomics analysis. While no significant associations were observed for most glycan models (fucosylation, p=0.526; bisecting GlcNAc, p=0.069; and sialylation, p=0.058), we discovered sex showed a potentially influential effect on galactosylation (p=0.001) (Supplementary files 5-8). These results suggest that while most glycan features appear unaffected by the examined covariates, galactosylation may be subject to sex-specific biological regulation." (Page 7, lines 153-160).

(6) The manuscript states that there are limited studies on antibody glycosylation in the context of HFRS, but does not cite any relevant literature. If prior work exists, it should be cited to contextualize the current study. If no prior studies have been conducted/reported, to the author's knowledge, that should be stated explicitly to show the novelty of the work.

Thank you for your suggestion. To our knowledge, there has been no prior reports regarding the regulation of IgG glycosylation in HFRS, particularly in relation to seroconversion. We have reworded this sentence in the revised manuscript. "Importantly, there have not been prior studies specifically examining plasma IgG N-glycome profiles derived from chromatographic peak data in HFRS patients, particularly in relation to seroconversion status. This gap in our knowledge motivated our systematic investigation of both total and virus-specific IgG glycosylation dynamics during acute infection." Please see the Introduction (Page 5, lines 92-96).

Reviewer #2 (Recommendations for the authors):

Minor points:

(1) Line 47, 78: The use of the word 'However' appears to be an incorrect expression.

We have made this correction.

(2) Line 127: The term 'glycome' should be replaced with 'N-glycome,' and all relevant expressions should be corrected accordingly, such as 'N-glycosylation.

We have made this correction.

(3) Line 84-87: The sentence 'A total of 166 HFRS patients...' contains a grammatical error.

We have made tis correction (Page 5, lines 99-101).

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Reply to the reviewers

Reviewer #1

Summary:

Miyamoto et al. report that importin α1 is highly enriched in a subfraction of micronuclei (about 40%), which exhibit defective nuclear envelopes and compromised accessibility of factors essential for the damage response associated with homologous recombination DNA repair. The authors suggest that the unequal localization and abnormal distribution of importin α1 within these micronuclei contribute to the genomic instability observed in cancer.

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Major comments:

1.) It is crucial to quantitatively assess the localization of importin α1 in micronuclei (MN) across non-transformed MCM10A cells compared to transformed cell lines (MC7, HeLa, and MDA-MB-231). This analysis would help determine whether the localization of importin α1 in MN correlates with genomic stability in human cancer cells

We appreciate the reviewer's thoughtful suggestion to compare non-transformed and transformed cell lines to evaluate importin α1 localization in MN. Given that HeLa cells are derived from cervical cancer rather than the mammary epithelium, we considered it inappropriate to directly compare them with non-transformed mammary epithelial MCF10A cells. Therefore, HeLa cells were analyzed separately to assess the effects of reversine treatment on importin α1 localization. The results indicated no significant difference between the treated and untreated HeLa cells. (Supplemental Fig. S2F in the revised manuscript). Regarding the comparison between MCF10A and the two cancer cell lines, MCF7 and MDA-MB-231, the proportion of importin α1-positive MN did not significantly differ across the cell lines, regardless of reversine treatment (Supplemental Fig. S3B, Untreated: p = 0.9850 and 0.5533; Reversine: p = 0.2218 and 0.9392). These results suggest that there is no clear difference in the localization of importin α1 in MN between the transformed and non-transformed cell lines tested. However, we acknowledge that this does not exclude the possibility that importin α1 localization to MN is linked to genomic instability under specific conditions.

2.) While the authors provide some evidence indicating partial disruption of nuclear envelopes in MN (Figures 3 and S4), it is noteworthy that this phenomenon also occurs in importin α1-negative MN. Furthermore, according to the figure legends, the data presented in both figures stem from a single experiment. Current literature suggests that compromised nuclear envelope integrity is one of the major contributors to genomic instability, mediated through mechanisms such as chromothripsis and cGAS-STING-mediated inflammation arising from MN. Therefore, a more comprehensive quantification of nuclear envelope integrity-ideally comparing non-transformed MCM10A cells with transformed cell lines (MC7, HeLa, and MDA-MB-231)-is necessary to substantiate the connection between aberrant importin α1 behavior in MN and chromothripsis processes, as well as regulation of the cGAS-STING pathway linked to genomic instability in cancer cells.

We thank the reviewer for the constructive suggestion to quantify nuclear envelope integrity more comprehensively. In response, we compared laminB1 localization at the MN membrane between importin α1-positive and -negative MN in MCF10A, MCF7, MDA-MB-231, and HeLa cells, and included these results in the revised manuscript (Fig. 4C). For each cell, the laminB1 intensity in the MN was normalized to that of the primary nucleus (PN). This analysis showed that laminB1 intensity was significantly lower in importin α1-positive MN across all cell lines, including non-transformed MCF10A cells. These findings support a close association between aberrant importin α1 accumulation and compromised nuclear envelope integrity, a key factor potentially linking MN to chromothripsis and cGAS-STING-mediated genomic instability.

3.) The schematic illustration presented in Figure 8 does not adequately summarize all findings from this study nor does it clarify how the localization of importin α1 within MN might hypothetically influence genome stability. Although it is reasonable to propose that "importin α can serve as a molecular marker for characterizing the dynamics of MN" (Line 344), the authors assert (Line 325) that their findings, along with others, have "potential implications for the induction of chromothripsis processes and regulation of the cGAS-STING pathway in cancer cells." However, they fail to provide a clear or even hypothetical explanation regarding how their findings contribute to these molecular events. To address this gap, it would be essential for them to contextualize their results within existing literature that explores and links structural integrity deficits or aberrant DNA replication/damage responses in MN with chromothripsis and inflammation (e.g., PMID: 32601372; PMID: 32494070; PMID: 27918550; PMID: 28738408; PMID: 28759889).

We agree that the previous schematic illustration (former Fig. 8) did not adequately summarize our findings and may have overstated our conclusions. Accordingly, we have removed this figure from the revised manuscript.

To address the reviewer's concern, we performed additional analyses and included the results in the new Figure 8. These data show that, in addition to RAD51, both RPA2 and cGAS display mutually exclusive localization with importin α1 in MN. RPA2, a single-stranded DNA-binding protein, stabilizes damaged DNA and enables RAD51 filament assembly during homologous recombination repair. Previous studies have demonstrated that RPA2 accumulates in ruptured MN in a CHMP4B-dependent manner (PMID: 32601372). Likewise, cGAS is a cytosolic DNA sensor that localizes to ruptured MN and activates innate immune signaling through the cGAS-STING pathway, as widely reported (PMID: 28738408; 28759889; see also PMID: 32494070; 27918550).

Our findings suggest an alternative scenario: even when nuclear envelope rupture occurs, importin α1-positive MN may remain inaccessible to DNA repair and sensing factors such as RPA2 and cGAS. This supports the view that importin α1 defines a distinct MN subset, separate from those characterized by the canonical DNA damage response or innate immune signaling factors. Furthermore, our overexpression experiments with EGFP-importin α1 (Fig. 7G, 7H) raises the possibility that importin α1 enrichment may impede the recruitment of DNA-binding proteins.

Taken together, these results support the conclusion that importin α1 marks a unique MN state and provides a molecular framework for distinguishing between different MN environments. At the reviewer's suggestion, we have cited all the recommended references (PMID: 32601372, 32494070, 27918550, 28738408, and 28759889) in the revised manuscript to better contextualize our findings. We are grateful for the reviewer's thoughtful suggestions and literature recommendations, which helped us clarify the implications of our findings within the broader context of chromothripsis and cGAS-STING-mediated genomic instability.

4.) Fig. 4D does not support the idea that importin α1 is euchromatin enriched: H3K9me3, H3K4me3 and H3K37me3 seem to be all deeply blue.

We sincerely thank the reviewer for pointing out the important limitations of the original version of Fig. 4D, as also raised in minor comment #5. As the reviewer correctly noted, this figure was intended to demonstrate that importin-α1 preferentially localizes to euchromatin regions (H3K4me3 and H3K36me3) rather than heterochromatin (H3K9me3 and H3K27me3). However, we acknowledge that in the original figure, the predominantly blue tone of the heatmap made this interpretation unclear and that the Spearman's correlation coefficient for H3K36me3 was missing. In response, we have substantially revised the figure (now shown as Fig. 5E in the revised manuscript). Specifically, we improved the color scale for better visual distinction, added the missing Spearman's coefficients for H3K36me3, and strengthened the analysis by incorporating ChIP-seq data obtained with two independent antibodies against importin α1 (Ab1 and Ab2). We believe that these revisions provide a clear and more accurate representation of euchromatin enrichment of importin-α1, as originally intended.

Indeed, the data presented by the authors do not adequately support a direct link between the presence of importin α1 in MN and genomic instability in human cancer cells. While the experimental correlations provided may not substantiate this connection definitively, they do lay a foundation for a grounded hypothesis and suggest the need for further research to explore this topic in greater depth. Additionally, it is worth noting that the evidence contributes to the growing list of nuclear proteins exhibiting abnormal behavior in micronuclei (MN). This highlights the significance of studying such proteins to understand their roles in genomic stability and cancer progression.

Following the reviewer's suggestion, we carefully revised the manuscript to ensure that our statements are consistent with the scope of the data and do not overstate our conclusions. As part of this effort, we removed the schematic illustration (former Fig. 8), which might have overstated our findings, and refined the relevant text to prevent overinterpretation.

To our knowledge, this study is the first to report the specific accumulation of importin α in MN. Our results suggest a previously unrecognized function of importin α beyond its canonical transport role and add to the growing list of nuclear proteins that exhibit abnormal behavior in MN. We hope that these findings will provide a conceptual and experimental basis for future studies aimed at clarifying the biological significance of MN heterogeneity and quality control in cancer biology.

Additional experiments are necessary to quantitatively assess the localization of importin α1 in micronuclei (MN) across non-transformed MCM10A cells and transformed cell lines (MC7, HeLa, MDA-MB-231). This analysis would help determine whether the localization of importin α1 in MN correlates with genomic stability in human cancer cells.

As part of our response to Major Comment 1, we conducted additional experiments to quantitatively compare importin α1 localization in MN between non-transformed MCF10A cells, breast cancer cell lines (MCF7 and MDA-MB-231), and HeLa cells. These results have been included in the revised manuscript (Supplemental Fig. S2F and Fig. S3B). The analyses showed no significant differences in the proportion of importin α1-positive MN among these cell lines, consistent with the reviewer's request for a more comprehensive evaluation.

The authors claim that importin α1 preferentially localizes to euchromatic areas rather than heterochromatic regions within MN. While this assertion is supported by the immunofluorescence (IF) images presented in Figures 4A/B and S5A/B, it remains less clear for Figure S5C/B. To strengthen this claim, providing averages of IF distributions from multiple cells across independent experiments would be beneficial to draw more robust conclusions.

We have quantified the co-localization of importin α1 with the euchromatin marker H3K4me3 and the heterochromatin marker H3K9me3 in micronuclei (MN) across four human cell lines (MCF10A, MCF7, MDA-MB-231, and HeLa). The results of this statistical analysis are included in the revised manuscript in Fig. 5C. These data provide quantitative evidence from independent experiments showing that importin α1 preferentially localizes to euchromatic regions within the MN, thereby supporting our initial observation.

Furthermore, ChIP-seq data are presented to support the idea that importin α1 preferentially distributes over euchromatin areas in MN. However, as described, the epigenetic chromatin status indicated by these ChIP-seq experiments reflects that of the principal nucleus (PN), not specifically the status within MN in MCF7 cells. Given that MN represent only a small fraction of the cell population under normal culture conditions-likely less than 5% for HeLa cells as shown in Figure S2D-the relevance of this data is limited. Additionally, according to data presented in Figure 1B, importin α1 does not localize or distribute within the PN as it does in MN in MCF7 cells. Therefore, further experiments should be conducted to substantiate that importin α1 preferentially targets euchromatin areas within MN and to compare this distribution with that observed in the principal nucleus. Such studies could reveal potential abnormalities regarding the correlation between epigenetic chromatin status and importin α distribution in MN.

As noted, these experiments were performed on whole-cell populations of MCF7 cells and therefore reflect the overall chromatin landscape, not specifically that of the MN. We fully acknowledge that MN constitute only a small fraction of the cell population under standard culture conditions (Supplemental Fig. S2D), and thus, the relevance of ChIP-seq data to MN must be interpreted with caution.

Nevertheless, our intention in presenting these data was to illustrate that importin α1 preferentially associates with euchromatin regions marked by H3K4me3. To examine this more directly, we analyzed importin α1 localization in MN using immunofluorescence with histone modification markers across multiple cell lines. These analyses, together with the quantitative results now included in the revised manuscript (Fig. 5C), confirming that importin α1 preferentially localizes to euchromatic regions within MN.

Taken together, although the ChIP-seq data were derived from whole-cell populations, the combined results from IF imaging and quantitative analysis support our interpretation that importin α1 retains its euchromatin-associating property within MN. We hope that these additional data will address the reviewer's concerns.

To support the hypothesis that importin α1 inhibits RAD51 accessibility within MN, Figures 7D and E should be supplemented with thorough quantification and statistical analysis based on at least three independent experiments. This additional data would enhance confidence in their findings regarding RAD51 accessibility inhibition by importin α1.

Following the reviewer's suggestion, we have added a new graph (Fig. 7F) in the revised manuscript. This figure presents the quantified frequency of RAD51-positive MN among importin α1-negative and importin α1-positive MN, analyzed across six microscopy fields (n = 6) from three independent experiments.

To improve clarity and consistency, we reorganized the panels: representative RAD51 images are now shown in Fig. 7B, and the Cell #1 (low RAD51) vs. Cell #2 (high RAD51) classification with etoposide responsiveness is summarized in Fig. 7C. As illustrated in Figs. 7D and 7E, importin α1 and RAD51 exhibit mutually exclusive localization in MN. Fig. 7F provides a unified statistical summary at the population level.

The results showed that the proportion of RAD51-positive MN was significantly lower among importin α1-positive MN than among importin α1-negative MN, providing robust quantitative support for the proposed mutual exclusivity between importin α1 localization and RAD51 accessibility in MN.

We are grateful to the reviewer for this constructive suggestion, which helped us clarify and better support the central message of our study.

The additional experiments proposed are controls and direct comparisons using the same techniques and experimental designs used by the authors, so it is reasonable that the authors can carry them out within a realistic timeframe.

We appreciate the reviewer's thoughtful consideration of the feasibility of the additional experiments.

Given the importance of reproducibility and the need to evaluate results based on imaging and quantitation, I strongly recommend that the authors include a detailed description of the optical microscopy procedures utilized in their study. This should encompass imaging conditions, acquisition settings, and the specific equipment used. Providing this information will enhance transparency and facilitate reproducibility. For reference, some valuable guidance on essential parameters for reproducibility can be found in Heddleston et al. (2021) (doi:10.1242/jcs.254144). Incorporating these details will not only strengthen the manuscript but also support other researchers in reproducing the findings accurately.

Following the reviewer's suggestion, we have substantially revised the Materials and Methods sections in the main and supplemental manuscripts to provide detailed descriptions of the optical microscopy procedures, including the specifications of the imaging equipment, acquisition settings, and image processing parameters. These revisions follow the best practices recommended by Heddleston et al. (2021, J. Cell Sci., doi:10.1242/jcs.254144).

We have also expanded the description of our quantitative image analysis using ImageJ, providing details on the parameters for MN identification and the measurement of colocalization rates between importin α and histone modifications. These additions ensured reproducibility and clarity.

We believe that these modifications will enhance the reproducibility of our results and increase the value of our study for the research community. We sincerely appreciate the reviewer's helpful suggestions.

Many of the plots and values in the manuscript lack appropriate statistical analysis, including p-values, which are not detailed in the figures or their legends. Furthermore, the Statistical Analysis section does not provide adequate information regarding the specific statistical tests employed or the criteria used to determine which analyses were applied in each case. To enhance the rigor and clarity of the study, it is essential that these issues be addressed prior to publication. A comprehensive presentation of statistical analysis will improve the reliability of the findings and allow readers to better understand the significance of the results. I recommend that the authors revise this section to include detailed explanations of all statistical methods used, along with corresponding p-values for all relevant comparisons.

We sincerely appreciate the reviewer's constructive comments highlighting the importance of transparent and rigorous statistical analyses. In response, we have carefully revised all figure panels, figure legends, and the Materials and Methods (Statistical Analysis) section in both the main and the supplementary manuscripts.

In the revised figure legends, we now provide the number of independent experiments and sample sizes (n), statistical tests applied (e.g., unpaired or paired two-tailed t-test, one-way ANOVA with Tukey's post-hoc test, two-way ANOVA with Sidak's multiple comparisons), data presentation format (mean {plus minus} SD), and corresponding p-values or significance indicators (*, **, ***). The Statistical Analysis section was also expanded to explain the rationale for selecting each statistical test, the criteria for significance, and the reporting of the replicates. These revisions ensure clarity, reproducibility, and transparency throughout the manuscript, directly addressing the reviewers' concerns. We are grateful for this valuable suggestion, which has significantly improved the rigor of our study.

Minor comments:

The authors claim that importin α1 exhibits remarkably low mobility in the micronuclei (MN) compared to its mobility in the principal nucleus (PN), as illustrated in Figure 1. However, based on the experimental design, this conclusion may not be appropriate. In the current setup, the FRAP experiment conducted in the PN measures the mobility of importin α1 molecules within the cell nucleus, where the influence of nuclear transport is likely negligible. Conversely, in the MN experiments shown, all molecules of importin α1 are bleached within a given MN. Consequently, what is being measured here primarily reflects the effects of nuclear transport rather than intrinsic molecular mobility. To accurately compare kinetics of nuclear transport, it would be essential to completely bleach the entire PN. If measuring molecular mobility between MN and PN is desired, only a small fraction of either MN or PN area/volume should be bleached during FRAP analysis. Additionally, it would be beneficial to include measurements of mobility for other canonical nuclear transport factors (e.g., RAN, CAS, RCC1) for comparative purposes. This broader context would allow for a more comprehensive understanding of importin α1 behavior relative to other factors involved in nuclear transport. Finally, utilizing cells that exhibit importin α1 signals in both PN and MN could further strengthen comparisons and provide more robust conclusions regarding its mobility dynamics.

We thank the reviewer for their constructive suggestions regarding our FRAP analysis. To address the concern that the original comparison between PN and the micronuclei (MN) might have been biased by differences in bleaching areas, we performed new experiments in which both PN and MN were fully bleached within the same cells (Fig. 3A, and 3C). This approach allowed for a more direct comparison of importin α1 dynamics under equivalent conditions.

These experiments revealed a markedly slower fluorescence recovery in MN than in PN, indicating reduced nuclear import and/or recycling efficiency of importin α1 in MN. In addition, we retained our original analysis to further characterize the heterogeneous mobility patterns of importin α1 in MN, identifying three distinct mobility classes: high, intermediate, and low (Fig. 3B, and 3D). Together, these results support our observation that importin α1 mobility is restricted in MN, likely due to altered nuclear transport dynamics.

As suggested by the reviewer, we attempted partial bleaching of MN to assess intranuclear mobility. However, owing to the small size of MN, partial bleaching is technically challenging and inconsistent, with some MN recovering even during the bleaching process. Therefore, reliable quantification was not possible. For transparency, these data are provided as a Reviewer-only Figure but were not included in the revised manuscript.

Finally, while we agree that examining other nuclear transport factors (e.g., RAN, CAS, RCC1) would be informative, our study focused on importin α1 dynamics. We consider these additional factors to be important directions for future investigations.

Prior studies are referenced appropriately in general, but the authors missed some references (PMID: 32601372; PMID: 32494070; PMID: 27918550; PMID: 28738408; PMID: 28759889) that I consider key to put the present findings in frame with previous works which link the lack of structural integrity and/or aberrant DNA replication/damage responses in MN with Cchromothripsis and inflammation.

We thank the reviewer for carefully pointing out the key references that are highly relevant to framing our findings in the context of previous studies on micronuclear instability, chromothripsis and inflammation. We fully agree with this suggestion.

In the revised manuscript, we have cited these studies in both the Introduction and Discussion sections. Specifically, we incorporated these studies when discussing the structural fragility of MN, aberrant DNA replication, and the exposure of micronuclear DNA to cytoplasmic sensors, which mechanistically link MN rupture to chromothripsis and cGAS-STING-mediated immune activation. For example, we now refer to the study demonstrating RPA2 recruitment to ruptured MN in a CHMP4B-dependent manner (PMID: 32601372), reports showing defective replication and DNA damage responses in MN (PMID: 32494070; 27918550), and seminal studies establishing cGAS localization to ruptured MN and activation of innate immune signaling (PMID: 28738408; 28759889).

By incorporating these references, we more clearly position our findings that importin α1 defines a distinct subset of MN lacking access to DNA repair and sensing factors such as RAD51, RPA2, and cGAS. This contextualization emphasizes that our data add to and extend the established view that compromised MN integrity underlies chromothripsis and inflammation by identifying importin α1 as a novel marker of an alternative MN microenvironment. We are grateful for this constructive recommendation, which has allowed us to strengthen the framing of our study in the existing literature.

The figures presented in the manuscript are clear; however, where plots are included, they require appropriate statistical analysis. It is essential to display p-values on the plots or within their legends to provide readers with information regarding the significance of the results. Including this statistical information will enhance the interpretability of the data and strengthen the overall findings of the study. I recommend that the authors revise these sections accordingly before publication.

In response, we have revised the relevant figure panels and their legends to clearly display the statistical significance, including p-values, where appropriate. Specifically, we added statistical annotations (p-values or significance markers such as asterisks) directly on the plots or in the corresponding legends, and clarified the number of replicates, statistical tests used, and definitions of error bars (mean {plus minus} SD). We believe that these revisions improve the interpretability and transparency of our results and strengthen the overall presentation of the data.

__ 1.) In lines 134-135, it is stated that "up to 40% of the MN showed importin α1 accumulation under both standard culture conditions and the reversine treatment (Fig. S2F)." However, Figure S2F only displays percentages for reversine-treated cells, and there is no mention in the text or figures regarding the percentage of importin α1-positive MN determined by immunofluorescence (IF) under standard culture conditions. This discrepancy should be addressed.__

Following the reviewer's comments, we revised Supplemental Fig. S2F shows a direct comparison of the proportion of importin α1-positive MN between untreated and reversine-treated HeLa cells based on indirect IF analysis. The Results section was updated accordingly (page 8, Lines 148-150): "We then examined whether reversine treatment affected the proportion of importin α1-positive MN. The results revealed that the MN formation rate for either untreated or treated cells was 36.2% {plus minus} 7.8 or 38.3% {plus minus} 8.8, respectively, with no significant difference (Fig. S2F). "

We believe that this revision addresses the reviewer's concern by providing relevant quantitative data for the untreated condition.

2.) In line 170, the authors state that "Cells in which overexpressed EGFP-importin α1 localized only in PN were excluded from the analysis (see Fig. 1E, top panels)." It is unclear why this exclusion was made. The authors should clarify whether they are referring to all constructs or only to the wild-type (WT) construct when mentioning EGFP-importin α1 localization solely in PN. This clarification is important as it may affect the results highlighted in line 173.

In this section, we aimed to clarify that the quantitative analysis focused exclusively on cells harboring MN, as the purpose of the analysis was to compare the localization of EGFP-importin α1 between MN and PN. We excluded cells that contained no MN and showed EGFP-importin α1 localization only in the PN. This criterion was consistently applied to both wild-type and mutant constructs. To avoid confusion, we have removed the sentence "Cells in which overexpressed EGFP-importin α1 localized only in PN were excluded from the analysis (see Fig. 1E, top panels)." from the revised manuscript.

3.) The statement in line 191 ("However, this antibody could not be further used in this context due to cross-reactivity with highly concentrated importin α1 in MN (Fig. S4)") is somewhat misleading. While it hints at a technical issue, it does not provide additional relevant information for understanding its implications for the rationale of the research. Moreover, Figure S4 is referenced but appears to refer specifically to panels S4D and E, which are not mentioned in the text. I recommend clarifying this point or removing it altogether.