Reviewer #2 (Public review):

Summary:

The authors tested tactile acuity on the breast of females using several tasks.

Results:

Tactile acuity, assessed by just-noticeable differences in judging whether a touch was above or below a comparison stimulus, was lower on both the lateral and medial breast than on the hand and back. Acuity also scaled inversely with breast size, echoing earlier findings that larger hands exhibit lower acuity, presumably because a similar number of tactile receptors must be distributed over larger or smaller body surfaces. Observing this principle in the breast as on the hand strengthens the view that fixed innervation is a general organizing principle of the tactile system. Both methodology and analysis appear sound.

Most participants were unable to localize touch to a specific quadrant of the nipple, suggesting it is perceived as a single tactile unit. However, the study does not address whether touches to the nipple and areola are confused; conceptualizing the nipple as a perceptual (landmark) unit would suggest that such confusion should not take place. Aside from this limitation, the methodology and analysis appear sound.

Absolute touch localization, assessed by asking participants to indicate locations on a 3D rendering of their own torso, revealed a bias toward the nipple. The authors interpret this as evidence that the nipple serves as a landmark attracting perceived touch. However, as reviewers noted during review, alternative explanations cannot be fully ruled out: because the stimulus array was centered on the nipple, the observed bias may stem from stimulus distribution rather than landmark status. Aside from this caveat, the methodology and analysis appear sound.

Overall assessment:

The study offers a welcome exception to the prevailing bias in tactile research that limits investigation to the hand and arm. Its support for the fixed innervation hypothesis and its suggestion that the nipple may serve as a potential landmark-though requiring further scrutiny-illustrate the value of extending research to other body regions. By employing multiple tasks, the authors address several key aspects of tactile perception and create links to earlier findings.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

The statistically adequate way of testing the biases is a hierarchical regression model (LMM) with a distance of the physical location from the nipple as a predictor, and a distance of the reported location from the nipple as a dependent variable. Either variable can be unsigned or signed for greater power, for example, coding the lateral breast as negative and the medial breast as positive. The bias will show in regression coefficients smaller than 1.

Thank you for this suggestion. We have subsequently replaced the relevant ANOVA analyses with LMM analyses. Specifically, we use an LMM for breast and back separately to show the different effects of distance, then use a combined LMM to compare the interaction. Finally, we use an LMM to assess the differences between precision and bias on the back and breast. The new analysis confirms earlier statements and do not change the results/interpretation of the data.

Moreover, any bias towards the nipple could simply be another instance of regression to the mean of the stimulus distribution, given that the tested locations were centered on the nipple. This confound can only be experimentally solved by shifting the distribution of the tested locations. Finally, given that participants indicated the locations on a 3D model of the body part, further experimentation would be required to determine whether there is a perceptual bias towards the nipple or whether the authors merely find a response bias.

A localization bias toward the nipple in this context does not show that the nipple is the anchor of the breast's tactile coordinate system. The result might simply be an instance of regression to the mean of the stimulus distribution (also known as experimental prior). To convincingly show localization biases towards the nipple, the tested locations should be centered at another location on the breast.

Another problem is the visual salience of the nipple, even though Blender models were uniformly grey. With this type of direct localization, it is very difficult to distinguish perceptual from response biases even if the regression to the mean problem is solved. There are two solutions to this problem: 1) Varying the uncertainty of the tactile spatial information, for example, by using a pen that exerts lighter pressure. A perceptual bias should be stronger for more uncertain sensory information; a response bias should be the same across conditions. 2) Measure bias with a 2IFC procedure by taking advantage of the fact that sensory information is noisier if the test is presented before the standard.

We believe that the fact that we explicitly tested two locations with equally distributed test locations, both of which had landmarks, makes this unlikely. Indeed, testing on the back is exactly what the reviewer suggests. It would also be impossible to test this “on another location on the breast” as we are sampling across the whole breast. Moreover, as markers persisted on the model within each block, the participants were generating additional landmarks on each trial. Thus, if there were any regression to the mean, this would be observed for both locations. Nevertheless, we recognize that this test cannot distinguish between a sensory bias towards the nipple and consistent response bias that is always in the direction of the nipple, though to what extent these are the same thing is difficult to disentangle. That said, if we had restricted testing to half of the breast such that the distribution of points was asymmetrical this would allow us to test the hypothesis put forward by the reviewer. We recognize that this is a limitation of the data and have downplayed statements and added caveats accordingly.

We have changed the appropriate heading and text in the discussion to downplay the finding:

“Reports are biased towards the nipple”

“suggesting that the nipple plays a pivotal role in the mental representation of the breast.”

it might be harder to learn the range of locations on the back given that stimulation is not restricted to an anatomically defined region as it is the case for the breast.

We apologize for any confusion but the point distribution is identical between tasks, as described in the methods.

The stability of the JND differences between body parts across subjects is already captured in the analysis of the JNDs; the ANOVA and the post-hoc testing would not be significant if the order were not relatively stable across participants. Thus, it is unclear why this is being evaluated again with reduced power due to improper statistics.

We apologize for any confusion here. Only one ANOVA with post-hoc testing was performed on the data. The second parenthetical describing the test was perhaps redundant and confusing, so I have removed it.

“(Error! Reference source not found.A, B, 1-way ANOVA with Tukey’s HSD post-hoc t-test: p = 0.0284)”

The null hypothesis of an ANOVA is that at least one of the mean values is different from the others; adding participants as a factor does not provide evidence for similarity.

We agree with this statement and have removed the appropriate text.

The pairwise correlations between body parts seem to be exploratory in nature. Like all exploratory analyses, the question arises of how much potential extra insights outweigh the risk of false positives. It would be hard to generate data with significant differences between several conditions and not find any correlations between pairs of conditions. Thus, the a priori chance of finding a significant correlation is much higher than what a correction accounts for.

We broadly agree with this statement. However, we believe that the analyses were important to determine if participants were systematically more or less acute across body parts. Moreover, both the fact that we actually did not observe any other significant relationships and that we performed post-hoc correction imply that no false positives were observed. Indeed, in the one relationship that was observed, we would need to have an assumed FDR over 10x higher than the existing post hoc correction required implying a true relationship.

If the JND at mid breast (measured with locations centered at the nipple) is roughly the same size as the nipple, it is not surprising that participants have difficulty with the categorical localization task on the nipple but perform better than chance on the significantly larger areola.

We agree that it is not surprising given the previously shown data, however, the initial finding is surprising to many and this experiment serves to reinforce the previous finding.

Neither signed nor absolute localization error can be compared to the results of the previous experiments. The JND should be roughly proportional to the variance of the errors.

We apologize for any confusion, however we are not comparing the values, merely observing that the results are consistent.

Reviewer #2 (Public review):

I had a hard time understanding some parts of the report. What is meant by "broadly no relationship" in line 137?

We have removed the qualifier to simplify the text.

It is suggested that spatial expansion (which is correlated with body part size) is related between medial breast and hand - is this to say that women with large hands have large medial breast size? Nipple size was measured, but hand size was not measured, is this correct?

Correct. We have added text to state as such.

It is furthermore unclear how the authors differentiate medial breast and NAC. The sentence in lines 140-141 seems to imply the two terms are considered the same, as a conclusion about NAC is drawn from a result about the medial breast. This requires clarification.

Thank you for catching this, we have corrected it in the text.

Finally, given that the authors suspect that overall localization ability (or attention) may be overshadowed by a size effect, would not an analysis be adequate that integrates both, e.g. a regression with multiple predictors?

If the reviewer means that participants would be consistently “acute” then we believe that SF1 would have stronger correlations. Consequently, we see no reason to add “overall tactile acuity” as a predictor.

In the paragraph about testing quadrants of the nipple, it is stated that only 3 of 10 participants barely outperformed chance with a p < 0.01. It is unclear how a significant ttest is an indication of "barely above chance".

We have adjusted the text to clarify our meaning.

“On the nipple, however, participants were consistently worse at locating stimuli on the nipple than the breast (paired t-test, t = 3.42, p < 0.01) where only 3 of the 10 participants outperformed chance, though the group as a whole outperformed chance (Error! Reference source not found.B, 36% ± 13%; Z = 5.5, p < 0.01).”

The final part of the paragraph on nipple quadrants (starting line 176) explains that there was a trend (4 of 10 participants) for lower tactile acuity being related to the inability to differentiate quadrants. It seems to me that such a result would not be expected: The stated hypothesis is that all participants have the same number of tactile sensors in their nipple and areola, independent of NAC size. In this section, participants determine the quadrant of a single touch. Theoretically, all participants should be equally able to perform this task, because they all have the same number of receptors in each quadrant of nipple and areola. Thus, the result in Figure 2C is curious.

We agree that this result seemingly contradicts observations from the previous experiment, however we believe that it relates to the distinction between the ability to perform relative distinctions and absolute localizations. In the first experiment, the presentation of two sequential points provides an implicit reference whereas in the quadrant task there is no reference. With the results of the third experiment in mind, biases towards the nipple would effectively reduce the ability of participants to identify the quadrant. What this result may imply is that the degree of bias is greater for women with greater expansion. We have added text to the discussion to lay this out.

“This negative trend implicitly contradicts the previous result where one might expect equal performance regardless of size as the location of the stimuli was scaled to the size of the nipple and areola. However, given the absence of a reference point, systematic biases are more likely to occur and thus may reflect a relationship between localization bias and breast size.”

This section reports an Anova (line 193/194) with a factor "participant". This doesn't appear sensible. Please clarify. The factor distance is also unclear; is this a categorical or a continuous variable? Line 400 implies a 6-level factor, but Anovas and their factors, respectively, are not described in methods (nor are any of the other statistical approaches).

We believe this comment has been addressed above with our replacement of the ANOVA with an LMM. We have also added descriptions of the analysis throughout the methods.

The analysis on imprecision using mean pairwise error (line 199) is unclear: does pairwise refer to x/y or to touch vs. center of the nipple?

We have clarified this to now read:

“To measure the imprecision, we computed the mean pairwise distance between each of the reported locations for a given stimulus location and the mean reported location.”

p8, upper text, what is meant by "relative over-representation of the depth axis"? Does this refer to the breast having depth but the equivalent area on the back not having depth? What are the horizontal planes (probably meant to be singular?) - do you simply mean that depth was ignored for the calculation of errors? This seems to be implied in Figure 3AB.

This is indeed what we meant. We have attempted to clarify in the text.

“Importantly, given the relative over-representation of the depth axis for the breast, we only considered angles in the horizontal planes such that the shape of the breast did not influence the results.” Became:

“Importantly, because the back is a relatively flat surface in comparison to the breast, errors were only computed in the horizontal plane and depth was excluded when computing the angular error.”

Lines 232-241, I cannot follow the conclusions drawn here. First, it is not clear to a reader what the aim of the presented analyses is: what are you looking for when you analyze the vectors? Second, "vector strength" should be briefly explained in the main text. Third, it is not clear how the final conclusion is drawn. If there is a bias of all locations towards the nipple, then a point closer to the nipple cannot exhibit a large bias, because the nipple is close-by. Therefore, one would expect that points close to the nipple exhibit smaller errors, but this would not imply higher acuity - just less space for localizing anything. The higher acuity conclusion is at odds with the remaining results, isn't it: acuity is low on the outer breast, but even lower at the NAC, so why would it be high in between the two?

Thank you for pointing out the circular logic. We have replaced this sentence with a more accurate statement.

“Given these findings, we conclude that the breast has lower tactile acuity than the hand and is instead comparable to the back. Moreover, localization of tactile events to both the back and breast are inaccurate but localizations to the breast are consistently biased towards the nipple.”

The discussion makes some concrete suggestions for sensors in implants (line 283). It is not clear how the stated numbers were computed. Also, why should 4 sensors nipple quadrants receive individual sensors if the result here was that participants cannot distinguish these quadrants?

Thank you for catching this, it should have been 4 sensors for the NAC, not just the nipple. We have fixed this in the text.

I would find it interesting to know whether participants with small breast measurement delta had breast acuity comparable to the back. Alternatively, it would be interesting to know whether breast and back acuity are comparable in men. Such a result would imply that the torso has uniform acuity overall, but any spatial extension of the breast is unaccounted for. The lowest single participant data points in Figure 1B appear similar, which might support this idea.

We agree that this is an interesting question and as you point out, the data does indicate that in cases of minimal expansion acuity may be constant on the torso. However, in the comparison of the JNDs, post-hoc testing revealed no significant difference between the back and either breast region. Consequently, subsampling the group would result in the same result. We have added a sentence to the discussion stating this.

“Consequently, the acuity of the breast is likely determined initially by torso acuity and then any expansion.”

eLife Assessment

This valuable study reports that EEG recordings of the earliest stage of information processing in the human visual cortex can be used to predict subsequent choice responses. The findings provide novel, solid evidence for integrative processing in low-level sensory cortices, though the exact nature of the neural signals measured here requires some clarification. While some conceptual issues need to be addressed, the paper is likely to be of interest to neuroscientists interested in the contribution of early sensory signals to decision-making.

Reviewer #1 (Public review):

General assessment of the work:

In this manuscript, Mohr and Kelly show that the C1 component of the human VEP is correlated with binary choices in a contrast discrimination task, even when the stimulus is kept constant and confounding variables are considered in the analysis. They interpret this as evidence for the role V1 plays during perceptual decision formation. Choice-related signals in single sensory cells are enlightening because they speak to the spatial (and temporal) scale of the brain computations underlying perceptual decision-making. However, similar signals in aggregate measures of neural activity offer a less direct window and thus less insight into these computations. For example, although I am not a VEP specialist, it seems doubtful that the measurements are exclusively picking up (an unbiased selection of) V1 spikes. Moreover, although this is not widely known, there is in fact a long history to this line of work. In 1972, Campbell and Kulikowski ("The Visual Evoked Potential as a function of contrast of a grating pattern" - Journal of Physiology) already showed a similar effect in a contrast detection task (this finding inspired the original Choice Probability analyses in the monkey physiology studies conducted in the early 1990's). Finally, it is not clear to me that there is an interesting alternative hypothesis that is somehow ruled out by these results. Should we really consider that simple visual signals such as spatial contrast are *not* mediated by V1? This seems to fly in the face of well-established anatomy and function of visual circuits. Or should we be open to the idea that VEP measurements are almost completely divorced from task-relevant neural signals? Why would this be an interesting technique then? In sum, while this work reports results in line with several single-cell and VEP studies and perhaps is technically superior in its domain, I find it hard to see how these findings would meaningfully impact our thinking about the neural and computational basis of spatial contrast discrimination.

Summary of substantive concerns:

(1) The study of choice probability in V1 cells is more extensive than portrayed in the paper's introduction. In recent years, choice-related activity in V1 has also been studied by Nienborg & Cumming (2014), Goris et al (2017), Jasper et al (2019), Lange et al (2023), and Boundy-Singer et al (2025). These studies paint a complex picture (a mixture of positive, absent, and negative results), but should be mentioned in the paper's introduction.

(2) The very first study to conduct an analysis of stimulus-conditioned neural activity during a perceptual decision-making task was, in fact, a VEP study: Campbell and Kulikowski (1972). This study never gained the fame it perhaps deserves. But it would be appropriate to weave it into the introduction and motivation of this paper.

(3) What are interesting alternative hypotheses to be considered here? I don't understand the (somewhat implicit) suggestion here that contrast representations late in the system can somehow be divorced from early representations. If they were, they would not be correlated with stimulus contrast.

(4) I find the arguments about the timing of the VEP signals somewhat complex and not very compelling, to be honest. It might help if you added a simulation of a process model that illustrated the temporal flow of the neural computations involved in the task. When are sensory signals manifested in V1 activity informing the decision-making process, in your view? And how is your measure of neural activity related to this latent variable? Can you show in a simulation that the combination of this process and linking hypothesis gives rise to inverted U-shaped relationships, as is the case for your data?

Reviewer #2 (Public review):

Summary:

Mohr and Kelly report a high-density EEG study in healthy human volunteers in which they test whether correlations between neural activity in the primary visual cortex and choice behavior can be measured non-invasively. Participants performed a contrast discrimination task on large arrays of Gabor gratings presented in the upper left and lower right quadrants of the visual field. The results indicate that single-trial amplitudes of C1, the earliest cortical component of the visual evoked potential in humans, predict forced-choice behavior over and beyond other behavioral and electrophysiological choice-related signals. These results constitute an important advance for our understanding of the nature and flexibility of early visual processing.

Strengths:

(1) The findings suggest a previously unsuspected role for aggregate early visual cortex activity in shaping behavioral choices.

(2) The authors extend well-established methods for assessing covariation between neural signals and behavioral output to non-invasive EEG recordings.

(3) The effects of initial afferent information in the primary visual cortex on choice behavior are carefully assessed by accounting for a wide range of potential behavioral and electrophysiological confounds.

(4) Caveats and limitations are transparently addressed and discussed.

Weaknesses:

(1) It is not clear whether integration of contrast information across relatively large arrays is a good test case for decision-related information in C1. The authors raise this issue in the Discussion, and I agree that it is all the more striking that they do find C1 choice probability. Nevertheless, I think the choice of task and stimuli should be explained in more detail.

(2) In a similar vein, while C1 has canonical topographical properties at the grand-average level, these may differ substantially depending on individual anatomy (which the authors did not assess). This means that task-relevant information will be represented to different degrees in individuals' single-trial data. My guess is that this confound was mitigated precisely by choosing relatively extended stimulus arrays. But given the authors' impressive track record on C1 mapping and modeling, I was surprised that the underlying rationale is only roughly outlined. For example, given the topographies shown and the electrode selection procedure employed, I assume that the differences between upper and lower targets are mainly driven by stimulus arms on the main diagonal. Did the authors run pilot experiments with more restricted stimulus arrays? I do not mean to imply that such additional information needs to be detailed in the main article, but it would be worth mentioning.

(3) Also, the stimulus arrangement disregards known differences in conduction velocity between the upper and lower visual fields. While no such differences are evident from the maximal-electrode averages shown in Figure 1B, it is difficult to assess this issue without single-stimulus VEPs and/or a dedicated latency analysis. The authors touch upon this issue when discussing potential pre-C1 signals emanating from the magnocellular pathway.

(4) I suspect that most of these issues are at least partly related to a lack of clarity regarding levels of description: the authors often refer to 'information' contained in C1 or, apparently interchangeably, to 'visual representations' before, during, or following C1. However, if I understand correctly, the signal predicting (or predicted by) behavioral choice is much cruder than what an RSA-primed readership may expect, and also cruder than the other choice-predictive signals entered as control variables: namely, a univariate difference score on single-trial data integrated over a 10 ms window determined on the basis of grand-averaged data. I think it is worth clarifying and emphasizing the nature of this signal as the difference of aggregate contrast responses that *can* only be read out at higher levels of the visual system due to the limited extent of horizontal connectivity in V1. I do not think that this diminishes the importance of the findings - if anything, it makes them more remarkable.

(5) Arguably even more remarkable is the finding that C1 amplitudes themselves appear to be influenced by choice history. The authors address this issue in the Discussion; however, I'm afraid I could not follow their argument regarding preparatory (and differential?) weighting of read-outs across the visual hierarchy. I believe this point is worth developing further, as it bears on the issue of whether C1 modulations are present and ecologically relevant when looking (before and) beyond stimulus-locked averages.

eLife Assessment

This study shows that excitatory cholecystokinin (CCK)-expressing neurons in hippocampal area CA3 influence hippocampal-dependent memory using multiple methods to manipulate excitatory CCK-expressing CA3 neurons selectively. The work is valuable because most past studies of CCK-expressing neurons have focused on those neurons that co-express CCK and GABA. Currently, the strength of evidence is incomplete; however, if additional evidence were to be presented that the methods were selective, the evaluation would potentially be higher.

Reviewer #1 (Public review):

Summary:

CCK is the most abundant neuropeptide in the brain, and many studies have investigated the role of CCK and inhibitory CCK interneurons in modulating neural circuits, especially in the hippocampus. The manuscript presents interesting questions regarding the role of excitatory CCK+ neurons in the hippocampus, which has been much less studied compared to the well-known roles of inhibitory CCK neurons in regulating network function. The authors adopt several methods, including transgenic mice and viruses, optogenetics, chemogenetics, RNAi, and behavioral tasks to explore these less-studied roles of excitatory CCK neurons in CA3. They find that the excitatory CCK neurons are involved in hippocampal-dependent tasks such as spatial learning and memory formation, and that CCK-knockdown impairs these tasks.

However, these questions are very dependent on ensuring that the study is properly targeting excitatory CCK neurons (and thus their specific contributions to behavior).

There needs to be much more characterization of the CCK transgenic mice and viruses to confirm the targeting. Without this, it is unclear whether the study is looking at excitatory CCK neurons or a more general heterogeneous CCK neuron population.

Strengths:

This field has focused mainly on inhibitory CCK+ interneurons and their role in network function and activity, and thus, this manuscript raises interesting questions regarding the role of excitatory CCK+ neurons, which have been much less studied.

Weaknesses:

(1a) This manuscript is dependent on ensuring that the study is indeed investigating the role of excitatory CCK-expressing neurons themselves and their specific contribution to behavior. There needs to be much more characterization of the CCK-expressing mice (crossed with Ai14 or transduced with various viruses) to confirm the excitatory-cell targeting. Without this, it is unclear whether the study is looking at excitatory CCK neurons or a more general heterogeneous CCK neuron population.

(1b) For the experiments that use a virus with the CCK-IRES-Cre mouse, there is no information or characterization on how well the virus targets excitatory CCK-expressing neurons. (Additionally, it has been reported that with CaMKIIa-driven protein expression, using viruses, can be seen in both pyramidal and inhibitory cells.)

(2) The methods and figure legends are extremely sparse, leading to many questions regarding methodology and accuracy. More details would be useful in evaluating the tools and data. More details would be useful in evaluating the tools and data. Additionally, further quantification would be useful-e.g. in some places, only % values are noted, or only images are presented.

(3) It is unclear whether the reduced CCK expression is correlated, or directly causing the impairments in hippocampal function. Does the CCK-shRNA have any additional detrimental effects besides affecting CCK-expression (e.g., is the CCK-shRNA also affecting some other essential (but not CCK-related) aspect of the neuron itself?)? Is there any histology comparison between the shRNA and the scrambled shRNA?

Reviewer #2 (Public review):

Summary:

In this study, the authors have demonstrated, through a comprehensive approach combining electrophysiology, chemogenetics, fiber photometry, RNA interference, and multiple behavioral tasks, the necessity of projections from CCK+ CAMKIIergic neurons in the hippocampal CA3 region to the CA1 region for regulating spatial memory in mice. Specifically, authors have shown that CA3-CCK CAMKIIergic neurons are selectively activated by novel locations during a spatial memory task. Furthermore, authors have identified the CA3-CA1 pathway as crucial for this spatial working memory function, thereby suggesting a pivotal role for CA3 excitatory CCK neurons in influencing CA1 LTP. The data presented appear to be well-organized and comprehensive.

Strengths:

(1) This work combined various methods to validate the excitatory CCK neurons in the CA3 area; these data are convincing and solid.

(2) This study demonstrated that the CA3-CCK CAMKIIergic neurons are involved in the spatial memory tasks; these are interesting findings, which suggest that these neurons are important targets for manipulating the memory-related diseases.

(3) This manuscript also measured the endogenous CCK from the CA3-CCK CAMKIIergic neurons; this means that CCK can be released under certain conditions.

Weaknesses:

(1) The authors do not mention which receptors of the CCK modulate these processes.

(2) This author does not test the CCK gene knockout mice or the CCK receptor knockout mice in these neural processes.

(3) The author does not test the source of CCK release during the behavioral tasks.

Reviewer #3 (Public review):

Summary:

Fengwen Huang et al. used multiple neuroscience techniques (transgenetic mouse, immunochemistry, bulk calcium recording, neural sensor, hippocampal-dependent task, optogenetics, chemogenetics, and interfer RNA technique) to elucidate the role of the excitatory cholecystokinin-positive pyramidal neurons in the hippocampus in regulating the hippocampal functions, including navigation and neuroplasticity.

Strengths:

(1) The authors provided the distribution profiles of excitatory cholecystokinin in the dorsal hippocampus via the transgenetic mice (Ai14::CCK Cre mice), immunochemistry, and retrograde AAV.

(2) The authors used the neural sensor and light stimulation to monitor the CCK release from the CA3 area, indicating that CCK can be secreted by activation of the excitatory CCK neurons.

(3) The authors showed that the activity of the excitatory CCK neurons in CA3 is necessary for navigation learning.

(4) The authors demonstrated that inhibition of the excitatory CCK neurons and knockdown of the CCK gene expression in CA3 impaired the navigation learning and the neuroplasticity of CA3-CA1 projections.

Weaknesses:

(1) The causal relationship between navigation learning and CCK secretion?

(2) The effect of overexpression of the CCK gene on hippocampal functions?

(3) What are the functional differences between the excitatory and inhibitory CCK neurons in the hippocampus?

(4) Do CCK sources come from the local CA3 or entorhinal cortex (EC) during the high-frequency electrical stimulation?

eLife Assessment

This study integrates large-scale behavioral, genetic, and molecular analyses in animal models to investigate morphine response. Utilizing high-quality, time-series Quantitative Trait Loci (QTL) mapping, the work provides compelling evidential support for novel, time-dependent genetic interactions (epistasis). A fundamental result of this rigorous analysis is the discovery of a novel Oprm1-Fgf12-MAPK signaling pathway, which offers new insights into the mechanisms of opioid sensitivity.

Reviewer #1 (Public review):

Summary:

The study by Lemen et al. represents a comprehensive and unique analysis of gene networks in rat models of opioid use disorder, using multiple strains and both sexes. It provides a time-series analysis of Quantitative Trait Loci (QTLs) in response to morphine exposure.

Strengths:

A key finding is the identification of a previously unknown morphine-sensitive pathway involving Oprm1 and Fgf12, which activates a cascade through MAPK kinases in D1 medium spiny neurons (MSNs). Strengths include the large-scale, multi-strain, sex-inclusive design, the time-series QTL mapping provides dynamic insights, and the discovery of an Oprm1-Fgf12-MAPK signaling pathway in D1 MSNs, which is novel and relevant.

Weaknesses:

(1) The proposed involvement of Nav1.2 (SCN2A) as a downstream target of the Oprm1-Fgf12 pathway requires further analysis/evidence. Is Nav1.2 (SCN2A) expressed in D1 neurons?

The authors mentioned that SCN8A (Nav1.6) was tested as a candidate mediator of Oprm1-Fgf12 loci and variation in locomotor activity. However, the proposed model supports SCN2A as a target rather than SCN8A. This is somewhat unexpected since SCN8A is highly abundant in MSN.

Can the authors provide expression data for SCN2A, Oprm1, and Fgf12 in D1 vs. D2 MSNs?

(2) The authors should consider adding a reference to FGF12 in Schizophrenia (PMC8027596) in the Introduction.

(3) There is recent evidence supporting the druggability of other intracellular FGFs, such as FGF14 (PMC11696184) and FGF13 (PMC12259270), through their interactions with Nav channels. What are the implications of these findings for drug discovery in the context of the present study? Could FGF12 be considered a potential druggable therapeutic target for opioid use disorder (OUD)?

Reviewer #2 (Public review):

Summary:

This highly novel and significant manuscript re-analyzes behavioral QTL data derived from morphine locomotor activity in the BXD recombinant inbred panel. The combination of interacting behavioral-pharmacology (morphine and naltrexone) time course data, high-resolution mouse genetic analyses, genetic analysis of gene expression (eQTLs), cross-species analysis with human gene expression and genetic data, and molecular modeling approaches with Bayesian network analysis produces new information on loci modulating morphine locomotor activity.

Furthermore, the identification of time-wise epistatic interactions between the Oprm1 and Fgf12 loci is highly novel and points to methodological approaches for identifying other epistatic interactions using animal model genetic studies.

Strengths:

(1) Use of state-of-the art genetic tools for mapping behavioral phenotypes in mouse models.

(2) Adequately powered analysis incorporating both sexes and time course analyses.

(3) Detection of time and sex-dependent interactions of two QTL loci modulating morphine locomotor activity.

(4) Identification of putative candidate genes by combined expression and behavioral genetic analyses.

(5) Use of Bayesian analysis to model causal interactions between multiple genes and behavioral time points.

Weaknesses:

(1) There is a need for careful editing of the text and figures to eliminate multiple typographical and other compositional errors.

(2) There are multiple examples of overstating the possible significance of results that should be corrected or at least directly pointed out as weaknesses in the Discussion. These include:

a) Assumption that the Oprm1 gene is the causal candidate gene for the major morphine locomotor Chr10 QTL at the early time epochs. Oprm1 is 400,000 bp away from the support interval of the Mor10a QTL locus, and there is no mention as to whether the Oprm1 mRNA eQTL overlaps with Mor10a.

b) Although the Bayesian analysis of possible complex interactions between Oprm1, Fgf12, other interacting genes, and behaviors is very innovative and produces testable hypotheses, a more straightforward mediation analysis of causal relationships between genotype, gene expression, and phenotype would have added strength to the arguments for the causal role of these individual genes.

c) The GWAS data analysis for Oprm1 and Fgf12 is incomplete in not mentioning actual significance levels for Oprm1 and perhaps overstating the nominal significance findings for Fgf12.

Appraisal:

The authors largely succeeded in reaching goals with novel findings and methodology.

Significance of Findings:

This study will likely spur future direct experimental studies to test hypotheses generated by this complex analysis. Additionally, the broad methodological approach incorporating time course genetic analyses may encourage other studies to identify epistatic interactions in mouse genetic studies.

Reviewer #3 (Public review):

Summary:

This is a clearly written paper that describes the reanalysis of data from a BXD study of the locomotor response to morphine and naloxone. The authors detect significant loci and an epistatic interaction between two of those loci. Single-cell data from outbred rats is used to investigate the interaction. The authors also use network methods and incorporate human data into their analysis.

Strengths:

One major strength of this work is the use of granular time-series data, enabling the identification of time-point-specific QTL. This allowed for the identification of an additional, distinct QTL (the Fgf12 locus) in this work compared to previously published analysis of these data, as well as the identification of an epistatic effect between Oprm1 (driving early stages of locomotor activation) and Fgf12 (driving later stages).

Weaknesses:

(1) What criteria were used to determine whether the epistatic interaction was significant? How many possible interactions were explored?

(2) Results are presented for males and females separately, but the decision to examine the two sexes separately was never explained or justified. Since it is not standard to perform GWAS broken down by sex, some initial explanation of this decision is needed. Perhaps the discussion could also discuss what (if anything) was learned as a result of the sex-specific analysis. In the end, was it useful?

(3) The confidence intervals for the results were not well described, although I do see them in one of the tables. The authors used a 1.5 support interval, but didn't offer any justification for this decision. Is that a 95% confidence interval? If not, should more consideration have been given to genes outside that interval? For some of the QTLs that are not the focus of this paper, the confidence intervals were very large (>10 Mb). Is that typical for BXDs?

eLife Assessment

This important study presents JABS, an open-source platform that integrates hardware and user-friendly software for standardized mouse behavioral phenotyping. The work has practical implications for improving reproducibility and accessibility in behavioral neuroscience, especially for linking behavior to genetics across diverse mouse strains. The strength of evidence is convincing, with comprehensive validation of the platform's components and enthusiastic reviewer support.

Reviewer #1 (Public review):

Summary:

This manuscript provides an open-source tool including hardware and software, and dataset to facilitate and standardize behavioral classification in laboratory mice. The hardware for behavioral phenotyping was extensively tested for safety. The software is GUI based facilitating the usage of this tool across the community of investigators that do not have a programming background. The behavioral classification tool is highly accurate, and the authors deposited a large dataset of annotations and pose tracking for many strains of mice. This tool has great potential for behavioral scientists that use mice across many fields, however there are many missing details that currently limit the impact of this tool and publication.

Strengths:

Software-hardware integration for facilitating cross-lab adaptation of the tool and minimizing the need to annotate new data for behavioral classification.

Data from many strains of mice was included in the classification and genetic analyses in this manuscript.

Large dataset annotated was deposited for the use of the community

GUI based software tool decreases barriers of usage across users with limited coding experience.

Weaknesses:

The GUI requires pose tracking for classification but, the software provided in JABS does not do pose tracking, so users must do pose tracking using a separate tool. The pose tracking quality directly impacts the classification quality, given that it is used for the feature calculation

Comments on revisions:

The authors addressed all my concerns.

Reviewer #2 (Public review):

Summary:

This manuscript presents the JAX Animal Behavior System (JABS), an integrated mouse phenotyping platform that includes modules for data acquisition, behavior annotation, and behavior classifier training and sharing. The manuscript provides details and validation for each module, demonstrating JABS as a useful open-source behavior analysis tool that removes barriers to adopting these analysis techniques by the community. In particular, with the JABS-AI module users can download and deploy previously trained classifiers on their own data, or annotate their own data and train their own classifiers. The JABS-AI module also allows users to deploy their classifiers on the JAX strain survey dataset and receive an automated behavior and genetic report.

Strengths:

(1) The JABS platform addresses the critical issue of reproducibility in mouse behavior studies by providing an end-to-end system from rig setup to downstream behavioral and genetic analyses. Each step has clear guidelines, and the GUIs are an excellent way to encourage best practices for data storage, annotation, and model training. Such a platform is especially helpful for labs without prior experience in this type of analysis.

(2) A notable strength of the JABS platform is its reuse of large amounts of previously collected data at JAX Labs, condensing this into pretrained pose estimation models and behavioral classifiers. JABS-AI also provides access to the strain survey dataset through automated classifier analyses, allowing large-scale genetic screening based on simple behavioral classifiers. This has the potential to accelerate research for many labs by identifying particular strains of interest.

(3) The ethograph analysis will be a useful way to compare annotators/classifiers beyond the JABS platform.

Weaknesses:

(1) The manuscript contains many assertions that lack references in both the Introduction and Discussion. For example, in the Discussion, the assertion "published research demonstrates that keypoint detection models maintain robust performance despite the presence of headstages and recording equipment" lacks reference.

(2) The provided GUIs lower the barrier to entry for labs that are just starting to collect and analyze mouse open field behavior data. However, users must run pose estimation themselves outside of the provided GUIs, which introduces a key bottleneck in the processing pipeline, especially for users without strong programming skills. The authors have provided pretrained pose estimation models and an example pipeline, which is certainly to be commended, but I believe the impact of these tools could be greatly magnified by an additional pose estimation GUI (just for running inference, not for labeling/training).

(3) While the manuscript does a good job of laying out best practices, there is an opportunity to further improve reproducibility for users of the platform. The software seems likely to perform well with perfect setups that adhere to the JABS criteria, but it is very likely there will be users with suboptimal setups - poorly constructed rigs, insufficient camera quality, etc. It is important, in these cases, to give users feedback at each stage of the pipeline so they can understand if they have succeeded or not. Quality control (QC) metrics should be computed for raw video data (is the video too dark/bright? are there the expected number of frames? etc.), pose estimation outputs (do the tracked points maintain a reasonable skeleton structure; do they actually move around the arena?), and classifier outputs (what is the incidence rate of 1-3 frame behaviors? a high value could indicate issues). In cases where QC metrics are difficult to define (they are basically always difficult to define), diagnostic figures showing snippets of raw data or simple summary statistics (heatmaps of mouse location in the open field) could be utilized to allow users to catch glaring errors before proceeding to the next stage of the pipeline, or to remove data from their analyses if they observe critical issues.

Comments on revisions:

I thank the authors for taking the time to address my comments. They have provided a lot of important context in their responses. My only remaining recommendation is to incorporate more of this text into the manuscript itself, as this context will also be interesting/important for readers (and potential users) to consider. Specifically:

the quality control/user feedback features that have already been implemented (these are extremely important, and unfortunately, not standard practice in many labs)

top-down vs bottom-up imaging trade-offs (you make very good points!)

video compression, spatial and temporal resolution trade-offs

more detail on why the authors chose pose-based rather than pixel-based classifiers

I believe the proposed system can be extremely useful for behavioral neuroscientists, especially since the top-down freely moving mouse paradigm is one of the most ubiquitous in the field. Many labs have reinvented the wheel here, and as a field it makes sense to coalesce around a set of pipelines and best practices to accelerate the science we all want to do. I make the above recommendation with this in mind: bringing together (properly referenced) observations and experiences of the authors themselves, as well as others in the field, provides a valuable resource for the community. Obviously, the main thrust of the manuscript should be about the tools themselves; it should not turn into a review paper, so I'm just suggesting some additional sentences/references sprinkled throughout as motivation for why the authors made the choices that they did.

Intro typo: "one link in the chainDIY rigs"

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

(1) The authors only report the quality of the classification considering the number of videos used for training, but not considering the number of mice represented or the mouse strain. Therefore, it is unclear if the classification model works equally well in data from all the mouse strains tested, and how many mice are represented in the classifier dataset and validation.

We agree that strain-level performance is critical for assessing generalizability. In the revision we now report per-strain accuracy and F1 for the grooming classifier, which was trained on videos spanning 60 genetically diverse strains (n = 1100 videos) and evaluated on the test set videos spanning 51 genetically diverse strains (n=153 videos). Performance is uniform across most strains (median F1 = 0.94, IQR = 0.899–0.956), with only modest declines in albino lines that lack contrast under infrared illumination; this limitation and potential remedies are discussed in the text. The new per-strain metrics are presented in the Supplementary figure (corresponding to Figure 4).

(2) The GUI requires pose tracking for classification, but the software provided in JABS does not do pose tracking, so users must do pose tracking using a separate tool. Currently, there is no guidance on the pose tracking recommendations and requirements for usage in JABS. The pose tracking quality directly impacts the classification quality, given that it is used for the feature calculation; therefore, this aspect of the data processing should be more carefully considered and described.

We have added a section to the methods describing how to use the pose estimation models used in JABS. The reviewer is correct that pose tracking quality will impact classification quality. We recommend that classifiers should only be re-used on pose files generated by the same pose models used in the behavior classifier training dataset. We hope that the combination of sharing classifier training data and making a more unified framework for developing and comparing classifiers will get us closer to having foundational behavior classification models that work in many environments. We also would like to emphasize that deviating from using our pose model will also likely hinder re-using our shared large datasets in JABS-AI (JABS1200, JABS600, JABS-BxD).

(3) Many statistical and methodological details are not described in the manuscript, limiting the interpretability of the data presented in Figures 4,7-8. There is no clear methods section describing many of the methods used and equations for the metrics used. As an example, there are no details of the CNN used to benchmark the JABS classifier in Figure 4, and no details of the methods used for the metrics reported in Figure 8.

We thank the reviewer for bringing this to our attention. We have added a methods section to the manuscript to address this concern. Specifically, we now provide: (1) improved citation visibility of the source of CNN experiments such that the reader can locate the architecture information, (2) mathematical formulations for all performance metrics (precision, recall, F1, …) with explicit equations;  (3) detailed statistical procedures including permutation testing methods, power analysis and multiple testing corrections used throughout Figures 7-8. These additions facilitate reproducibility and proper interpretation of all quantitative results presented in the manuscript.

Reviewer #2 (Public review):

(1) The manuscript as written lacks much-needed context in multiple areas: what are the commercially available solutions, and how do they compare to JABS (at least in terms of features offered, not necessarily performance)? What are other open-source options?

JABS adds to a list of commercial and open source animal tracking platforms. There are several reviews and resources that cover these technologies. JABS covers hardware, behavior prediction, a shared resource for classifiers, and genetic association studies. We’re not aware of another system that encompasses all these components. Commercial packages such as EthoVision XT and HomeCage Scan give users a ready-made camera-plus-software solution that automatically tracks each mouse and reports simple measures such as distance travelled or time spent in preset zones, but they do not provide open hardware designs, editable behavior classifiers, or any genetics workflow. At the open-source end, the >100 projects catalogued on OpenBehavior and summarised in recent reviews (Luxem et al., 2023; Işık & Ünal 2023) usually cover only one link in the chain—DIY rigs, pose-tracking libraries (e.g., DeepLabCut, SLEAP) or supervised and unsupervised behaviour-classifier pipelines (e.g., SimBA, MARS, JAABA, B-SOiD, DeepEthogram). JABS provides an open source ecosystem that integrates all four: (i) top-down arena hardware with parts list and assembly guide; (ii) an active-learning GUI that produces shareable classifiers; (iii) a public web service that enables sharing of the trained classifier and applies any uploaded classifier to a large and diverse strain survey; and (iv) built-in heritability, genetic-correlation and GWAS reporting. We have added a concise paragraph in the Discussion that cites these resources and makes this end-to-end distinction explicit.

(2) How does the supervised behavioral classification approach relate to the burgeoning field of unsupervised behavioral clustering (e.g., Keypoint-MoSeq, VAME, B-SOiD)? 

The reviewer raises an important point about the rapidly evolving landscape of automated behavioral analysis, where both supervised and unsupervised approaches offer complementary strengths for different experimental contexts. Unsupervised methods like Keypoint-MoSeq , VAME , and B-SOiD , which prioritize motif discovery from unlabeled data but may yield less precise alignments with expert annotations, as evidenced by lower F1 scores in comparative evaluations. Supervised approaches (like ours), by contrast, employ fully supervised classifiers to deliver frame-accurate, behavior-specific scores that align directly with experimental hypotheses. Ultimately, a pragmatic hybrid strategy, starting with unsupervised pilots to identify motifs and transitioning to supervised fine-tuning with minimal labels, can minimize annotation burdens and enhance both discovery and precision in ethological studies. This has been added in the discussion section of the manuscript.

(3) What kind of studies will this combination of open field + pose estimation + supervised classifier be suitable for? What kind of studies is it unsuited for? These are all relevant questions that potential users of this platform will be interested in.

This approach is suitable for a wide array of neuroscience, genetics, pharmacology, preclinical, and ethology studies. We have published in the domains of action detection for complex behaviors such as grooming, gait and posture, frailty, nociception, and sleep. We feel these tools are indispensable for modern behavior analysis. 

(4) Throughout the manuscript, I often find it unclear what is supported by the software/GUI and what is not. For example, does the GUI support uploading videos and running pose estimation, or does this need to be done separately? How many of the analyses in Figures 4-6 are accessible within the GUI?

We have now clarified these. The JABS framework comprises two distinct GUI applications with complementary functionalities. The JABS-AL (active learning) desktop application handles video upload, behavioral annotation, classifier training, and inference -- it does not perform pose estimation, which must be completed separately using our pose tracking pipeline (https://github.com/KumarLabJax/mouse-tracking-runtime). If a user does not want to use our pose tracking pipeline, we have provided conversions through SLEAP to convert to our JABS pose format.  The web-based GUI enables classifier sharing and cloud-based inference on our curated datasets (JABS600, JABS1200) and downstream behavioral statistics and genetic analyses (Figures 4-6). The JABS-AL application also supports CLI (command line interface) operation for batch processing.  We have clarified these distinctions and provided a comprehensive workflow diagram in the revised Methods section.

(5) While the manuscript does a good job of laying out best practices, there is an opportunity to further improve reproducibility for users of the platform. The software seems likely to perform well with perfect setups that adhere to the JABS criteria, but it is very likely that there will be users with suboptimal setups - poorly constructed rigs, insufficient camera quality, etc. It is important, in these cases, to give users feedback at each stage of the pipeline so they can understand if they have succeeded or not. Quality control (QC) metrics should be computed for raw video data (is the video too dark/bright? are there the expected number of frames? etc.), pose estimation outputs (do the tracked points maintain a reasonable skeleton structure; do they actually move around the arena?), and classifier outputs (what is the incidence rate of 1-3 frame behaviors? a high value could indicate issues). In cases where QC metrics are difficult to define (they are basically always difficult to define), diagnostic figures showing snippets of raw data or simple summary statistics (heatmaps of mouse location in the open field) could be utilized to allow users to catch glaring errors before proceeding to the next stage of the pipeline, or to remove data from their analyses if they observe critical issues.

These are excellent suggestions that align with our vision for improving user experience and data quality assessment. We recognize the critical importance of providing users with comprehensive feedback at each stage of the pipeline to ensure optimal performance across diverse experimental setups. Currently, we provide end-users with tools and recommendations to inspect their own data quality. In our released datasets (Strain Survey OFA and BXD OFA), we provide video-level quality summaries for coverage of our pose estimation models. 

For behavior classification quality control, we employ two primary strategies to ensure proper operation: (a) outlier manual validation and (b) leveraging known characteristics about behaviors. For each behavior that we predict on datasets, we manually inspect the highest and lowest expressions of this behavior to ensure that the new dataset we applied it to maintains sufficient similarity. For specific behavior classifiers, we utilize known behavioral characteristics to identify potentially compromised predictions. As the reviewer suggested, high incidence rates of 1-3 frame bouts for behaviors that typically last multiple seconds would indicate performance issues.

We currently maintain in-house post-processing scripts that handle quality control according to our specific use cases. Future releases of JABS will incorporate generalized versions of these scripts, integrating comprehensive QC capabilities directly into the platform. This will provide users with automated feedback on video quality, pose estimation accuracy, and classifier performance, along with diagnostic visualizations such as movement heatmaps and behavioral summary statistics.

Reviewer #1 (Recommendations for the authors):

(1) A weakness of this tool is that it requires pose tracking, but the manuscript does not detail how pose tracking should be done and whether users should expect that the data deposited will help their pose tracking models. There is no specification on how to generate pose tracking that will be compatible with JABS. The classification quality is directly linked to the quality of the pose tracking. The authors should provide more details of the requirements of the pose tracking (skeleton used) and what pose tracking tools are compatible with JABS. In the user website link, I found no such information. Ideally, JABS would be integrated with the pose tracking tool into a single pipeline. If that is not possible, then the utility of this tool relies on more clarity on which pose tracking tools are compatible with JABS.

The JABS ecosystem was deliberately designed with modularity in mind, separating the pose estimation pipeline from the active learning and classification app (JABS-AL) to offer greater flexibility and scalability for users working across diverse experimental setups. Our pose estimation pipeline is documented in detail within the new Methods subsection, outlining the steps to obtain JABS-compatible keypoints with our recommended runtime (https://github.com/KumarLabJax/mouse-tracking-runtime) and frozen inference models (https://github.com/KumarLabJax/deep-hrnet-mouse). This pipeline is an independent component within the broader JABS workflow, generating skeletonized keypoint data that are then fed into the JABS-AL application for behavior annotation and classifier training.

By maintaining this separation, users have the option to use their preferred pose tracking tools— such as SLEAP —while ensuring compatibility through provided conversion utilities to the JABS skeleton format. These details, including usage instructions and compatibility guidance, are now thoroughly explained in the newly added pose estimation subsection of our Methods section. This modular design approach ensures that users benefit from best-in-class tracking while retaining the full power and reproducibility of our active learning pipeline.

(2) The authors should justify why JAABA was chosen to benchmark their classifier. This tool was published in 2013, and there have been other classification tools (e.g., SIMBA) published since then.  

We appreciate the reviewer’s suggestion regarding SIMBA. However, our comparisons to JAABA and a CNN are based on results from prior work (Geuther, Brian Q., et al. "Action detection using a neural network elucidates the genetics of mouse grooming behavior." Elife 10 (2021): e63207.), where both were used to benchmark performance on our publicly released dataset. In this study, we introduce JABS as a new approach and compare it against those established baselines. While SIMBA may indeed offer competitive performance, we believe the responsibility to demonstrate this lies with SIMBA’s authors, especially given the availability of our dataset for benchmarking.

(3) I had a lot of trouble understanding the elements of the data calculated in JABS vs outside of JABS. This should be clarified in the manuscript.

(a) For example, it was not intuitive that pose tracking was required and had to be done separately from the JABS pipeline. The diagrams and figures should more clearly indicate that.

(b) In section 2.5, are any of those metrics calculated by JABS? Another software GEMMA, but no citation is provided for this tool. This created ambiguity regarding whether this is an analysis that is separate from JABS or integrated into the pipeline.  

We acknowledge the confusion regarding the delineation between JABS components and external tools, and we have comprehensively addressed this throughout the manuscript. The JABS ecosystem consists of three integrated modules: JABS-DA (data acquisition), JABS-AL (active learning for behavior annotation and classifier training), and JABS-AI (analysis and integration via web application). Pose estimation, while developed by our laboratory, operates as a preprocessing pipeline that generates the keypoint coordinates required for subsequent JABS classifier training and annotation workflows. We have now added a dedicated Methods subsection that explicitly maps each analytical step to its corresponding software component, clearly distinguishing between core JABS modules and external tools (such as GEMMA for genetic analysis). Additionally, we have provided proper citations and code repositories for all external pipelines to ensure complete transparency regarding the computational workflow and enable full reproducibility of our analyses.

(4) There needs to be clearer explanations of all metrics, methods, and transformations of the data reported.

(a) There is very little information about the architecture of the classification model that JABS uses.

(b) There are no details on the CNN used for comparing and benchmarking the classifier in JABS.

(c) Unclear how the z-scoring of the behavioral data in Figure 7 was implemented.

(d) There is currently no information on how the metrics in Figure 8 are calculated.

We have added a comprehensive Methods section that not only addresses the specific concerns raised above but provides complete methodological transparency throughout our study. This expanded section includes detailed descriptions of all computational architectures (including the JABS classifier and grooming benchmark models and metrics), statistical procedures and data transformations (including the z-scoring methodology for Figure 7), downstream genetic analysis (including all measures presented in Figure 8), and preprocessing pipelines. 

(5) The authors talk about their datasets having visual diversity, but without seeing examples, it is hard to know what they mean by this visual diversity. Ideally, the manuscript would have a supplementary figure with a representation of the variety of setups and visual diversity represented in the datasets used to train the model. This is important so that readers can quickly assess from reading the manuscript if the pre-trained classifier models could be used with the experimental data they have collected.

The visual diversity of our training datasets has been comprehensively documented in our previous tracking work (https://www.nature.com/articles/s42003-019-0362-1), which systematically demonstrates tracking performance across mice with diverse coat colors (black, agouti, albino, gray, brown, nude, piebald), body sizes including obese mice, and challenging recording conditions with dynamic lighting and complex environments. Notably, Figure 3B in that publication specifically illustrates the robustness across coat colors and body shapes that characterize the visual diversity in our current classifier training data. To address the reviewer's concern and enable readers to quickly assess the applicability of our pre-trained models to their experimental data, we have now added this reference to the manuscript to ground our claims of visual diversity in published evidence.

(6) All figures have a lot of acronyms used that are not defined in the figure legend. This makes the figures really hard to follow. The figure legends for Figures 1,2, 7, and 9 did not have sufficient information for me to comprehend the figure shown.

We have fixed this in the manuscript. 

(7) In the introduction, the authors talk about compression artifacts that can be introduced in camera software defaults. This is very vague without specific examples.

This is a complex topic that balances the size and quality of video data and is beyond the scope of this paper. We have carefully optimized this parameter and given the user a balanced solution. A more detailed blog post on compression artifacts can be found at our lab’s webpage (https://www.kumarlab.org/2018/11/06/brians-video-compression-tests/). We have also added a comment about keyframes shifting temporal features in the main manuscript. 

(8) More visuals of the inside of the apparatus should be included as supplementary figures. For example, to see the IR LEDs surrounding the camera.

We have shared data from JABS as part of several papers including the tracking paper (Geuther et al 2019), grooming, gait and posture, mouse mass. We have also released entire datasets that as part of this paper (JABS1800, JABS-BXD). We also have step by step assembly guide that shows the location of the lights/cameras and other parts (see Methods, JABS workflow guide, and this PowerPoint file in the GitHub repository (https://github.com/KumarLabJax/JABS-datapipeline/blob/main/Multi-day%20setup%20PowerPoint%20V3.pptx).

(9) Figure 2 suggests that you could have multiple data acquisition systems simultaneously. Do each require a separate computer? And then these are not synchronized data across all boxes?

Each JABS-DA unit has its own edge device (Nvidia Jetson). Each system (which we define as multiple JABS-DA areas associated with one lab/group) can have multiple recording devices (arenas). The system requires only 1 control portal (RPi computer) and can handle as many recording devices as needed (Nvidia computer w/ camera associated with each JABS-DA arena). To collect data, 1 additional computer is needed to visit the web control portal and initiate a recording session. Since this is a web portal, users can use any computer or a tablet. The recording devices are not strictly synchronized but can be controlled in a unified manner.

(10) The list of parts on GitHub seems incomplete; many part names are not there.

We thank referee for bringing this to our attention. We have updated the GitHub repository (and its README) which now links out to the design files. 

(11) The authors should consider adding guidance on how tethers and headstages are expected to impact the use of JABS, as many labs would be doing behavioral experiments combined with brain measurements.

While our pose estimation model was not specifically trained on tethered animals, published research demonstrates that keypoint detection models maintain robust performance despite the presence of headstages and recording equipment. Once accurate pose coordinates are extracted, the downstream behavior classification pipeline operates independently of the pose estimation method and would remain fully functional. We recommend users validate pose estimation accuracy in their specific experimental setup, as the behavior classification component itself is agnostic to the source of pose coordinates.

Reviewer #2 (Recommendations for the authors):

(1) "Using software-defaults will introduce compression artifacts into the video and will affect algorithm performance." Can this be quantified? I imagine most of the performance hit comes from a decrease in pose estimation quality. How does a decrease in pose estimation quality translate to action segmentation? Providing guidelines to potential users (e.g., showing plots of video compression vs classifier performance) would provide valuable information for anyone looking to use this system (and could save many labs countless hours replicating this experiment themselves). A relevant reference for the effect of compression on pose estimation is Mathis, Warren 2018 (bioRxiv): On the inference speed and video-compression robustness of DeepLabCut.

Since our behavior classification approach depends on features derived from keypoint, changes in keypoint accuracy will affect behavior segmentation accuracy. We agree that it is important to try and understand this further, particularly with the shared bioRxiv paper investigating the effect of compression on pose estimation accuracy. Measuring the effect of compression on keypoint and behavior classification is a complex task to evaluate concisely, given the number of potential variables to inspect. To list a few variables that should be investigated are: discrete cosine transform quality (Mathis, Warren experiment), Frame Size (Mathis, Warren experiment), Keyframe Interval (new, unique to video data), inter-frame settings (new, unique to video data), behavior of interest, Pose models with compression-augmentation used in training ( https://arxiv.org/pdf/1506.08316?) and type of CNN used (under active development). The simplest recommendation that we can make at this time is that we know compression will affect behavior predictions and that users should be cautious about using our shared classifiers on compressed video data. To show that we are dedicated in sharing these results as we run those experiments, in a related work ( CV4Animals conference accepted paper (https://www.cv4animals.com/) and can be downloaded here https://drive.google.com/file/d/1UNQIgCUOqXQh3vcJbM4QuQrq02HudBLD/view) we have already begun to inspect how changing some factors affect behavior segmentation performance. In this work, we investigate the robustness of behavior classification across multiple behaviors using different keypoint subsets. Our findings in this work is that classifiers are relatively stable across different keypoint subsets. We are actively working on follow-up effort to investigate the effect of keypoint noise, CNN model architecture, and other factors we've listed above on behavior segmentation tasks.

(2) The analysis of inter-annotator variability is very interesting. I'm curious how these differences compare to two other types of variability:

(a) intra-annotator variability; I think this is actually hard to quantify with the presented annotation workflow. If a given annotator re-annotated a set of videos, but using different sparse subsets of the data, it is not possible to disentangle annotator variability versus the effect of training models on different subsets of data. This can only be rigorously quantified if all frames are labeled in each video.

We propose an alternative approach to behavior classifier development in the text associated with Figure 3C. We do not advocate for high inter-annotator agreement since individual behavior experts have differing labeling style (an intuitive understanding of the behavior). Rather, we allow multiple classifiers for the same behavior and allow the end user to prioritize classifiers based on heritability of the behavior from a classifier.  

(b) In lieu of this, I'd be curious to see the variability in model outputs trained on data from a single annotator, but using different random seeds or train/val splits of the data. This analysis would provide useful null distributions for each annotator and allow for more rigorous statistical arguments about inter-annotator variability. 

JABS allows the user to use multiple classifiers (random forest, XGBoost). We do not expect the user to carry out hyperparameter tuning or other forms of optimization. We find that the major increase in performance comes from optimizing the size of the window features and folds of cross validation. However, future versions of JABS-AL could enable a complete hyper-parameter scan across seeds and data splits to obtain a null distribution for each annotator. 

(c) I appreciate the open-sourcing of the video/pose datasets. The authors might also consider publicly releasing their pose estimation and classifier training datasets (i.e., data plus annotations) for use by method developers.

We thank the referee for acknowledging our commitment to open data sharing practices. Building upon our previously released strain survey dataset, we have now also made our complete classifier training resources publicly available, including the experimental videos, extracted pose coordinates, and behavioral annotations. The repository link has been added to the manuscript to ensure full reproducibility and facilitate community adoption of our methods.  

(3) More thorough discussion on the limitations of the top-down vs bottom-up camera viewpoint; are there particular scientific questions that are much better suited to bottomup videos (e.g., questions about paw tremors, etc.).

Top-down imaging, bottom-up, and multi-view imaging have a variety of pros and cons. Generally speaking, multi-view imaging will provide the most accurate pose models but requires increased resources on both hardware setup as well as processing of data. Top-down provides the advantage of flexibility for materials, since the floor doesn’t need to be transparent. Additionally lighting and potential reflection with the bottom-up perspective. Since the paws are not occluded from the bottom-up perspective, models should have improved paw keypoint precision allowing the model to observe more subtle behaviors. However, the appearance of the arena floor will change over time as the mice defecate and urinate. Care must be taken to clean the arena between recordings to ensure transparency is maintained. This doesn’t impact top-down imaging that much but will occlude or distort from the bottom-up perspective. Additionally, the inclusion of bedding for longer recordings, which is required by IACUC, will essentially render bottom-up imaging useless because the bedding will completely obscure the mouse. Overall, while bottomup may provide a precision benefit that will greatly enhance subtle motion, top-down imaging is overall more robust for obtaining consistent imaging across large experiments for longer periods of time.

(4) More thorough discussion on what kind of experiments would warrant higher spatial or temporal resolution (e.g., investigating slight tremors in a mouse model of neurodegenerative disease might require this greater resolution).

This is an important topic that deserves its own perspective guide. We try to capture some of this in the paper on specifications. However, we only scratch the surface. Overall, there are tradeoffs between frame rate, resolution, color/monochrome, and compression. Labs have collected data at hundreds of frames per second to capture the kinetics of reflexive behavior for pain (AbdoosSaboor lab) or whisking behavior. Labs have also collected data a low 2.5 frames per second for tracking activity or centroid tracking (see Kumar et al PNAS). The data collection specifications are largely dependent on the behaviors being captured. Our rule of thumb is the Nyquist Limit, which states that the data capture rate needs to be twice that of the frequency of the event. For example, certain syntaxes of grooming occur at 7Hz and we need 14FPS to capture this data. JABS collects data at 30FPS, which is a good compromise between data load and behavior rate. We use 800x800 pixel resolution which is a good compromise to capture animal body parts while limiting data size. Thank you for providing the feedback that the field needs guidance on this topic. We will work on creating such guidance documents for video data acquisition parameters to capture animal behavior data for the community as a separate publication.

(5) References 

(a) Should add the following ref when JAABA/MARS are referenced: Goodwin et al.2024, Nat Neuro (SimBA)

(b) Could also add Bohnslav et al. 2021, eLife (DeepEthogram).

(c) The SuperAnimal DLC paper (Ye et al. 2024, Nature Comms) is relevant to the introduction/discussion as well.

We thank the referee for the suggestions. We have added these references.  

(6) Section 2.2:

While I appreciate the thoroughness with which the authors investigated environmental differences in the JABS arena vs standard wean cage, this section is quite long and eventually distracted me from the overall flow of the exposition; might be worth considering putting some of the more technical details in the methods/appendix.

These are important data for adopters of JABS to gain IACUC approval in their home institution. These committees require evidence that any new animal housing environment has been shown to be safe for the animals. In the development of JABS, we spent a significant amount of time addressing the JAX veterinary and IACUC concerns. Therefore, we propose that these data deserve to be in the main text. 

(7) Section 2.3.1:

(a) Should again add the DeepEthogram reference here

(b) Should reference some pose estimation papers: DeepLabCut, SLEAP, Lightning Pose. 

We thank the referee for the suggestions. We have added these references.  

(c) "Pose based approach offers the flexibility to use the identified poses for training classifiers for multiple behaviors" - I'm not sure I understand why this wouldn't be possible with the pixel-based approach. Is the concern about the speed of model training? If so, please make this clearer.

The advantage lies not just in training speed, but in the transferability and generalization of the learned representations. Pose-based approaches create structured, low-dimensional latent embeddings that capture behaviorally relevant features which can be readily repurposed across different behavioral classification tasks, whereas pixel-based methods require retraining the entire feature extraction pipeline for each new behavior. Recent work demonstrates that pose-based models achieve greater data efficiency when fine-tuned for new tasks compared to pixel-based transfer learning approaches [1], and latent behavioral representations can be partitioned into interpretable subspaces that generalize across different experimental contexts [2]. While pixel-based approaches can achieve higher accuracy on specific tasks, they suffer from the "curse of dimensionality" (requiring thousands of pixels vs. 12 pose coordinates per frame) and lack the semantic structure that makes pose-based features inherently reusable for downstream behavioral analysis.

(1) Ye, Shaokai, et al. "SuperAnimal pretrained pose estimation models for behavioral analysis." Nature communications 15.1 (2024): 5165.

(2) Whiteway, Matthew R., et al. "Partitioning variability in animal behavioral videos using semi-supervised variational autoencoders." PLoS computational biology 17.9 (2021): e1009439.  

(d) The pose estimation portion of the pipeline needs more detail. Do users use a pretrained network, or do they need to label their own frames and train their own pose estimator? If the former, does that pre-trained network ship with the software? Is it easy to run inference on new videos from a GUI or scripts? How accurate is it in compliant setups built outside of JAX? How long does it take to process videos?

We have added the guidance on pose estimation in the manuscript (section “2.3.1 Behavior annotation and classifier training” and in the methods section titled “Pose tracking pipeline”)

(e) The final paragraph describing how to arrive at an optimal classifier is a bit confusing - is this the process that is facilitated by the app, or is this merely a recommendation for best practices? If this is the process the app requires, is it indeed true that multiple annotators are required? While obviously good practice, I imagine there will be many labs that just want a single person to annotate, at least in the beginning prototyping stages. Will the app allow training a model with just a single annotator?

We have clarified this in the text. 

(8) Section 2.5:

(a) This section contained a lot of technical details that I found confusing/opaque, and didn't add much to my overall understanding of the system; sec 2.6 did a good job of clarifying why 2.5 is important. It might be worth motivating 2.5 by including the content of 2.6 first, and moving some of the details of 2.5 to the method/appendix.

We moved some of the technical details in section 2.5 to the methods section titled “Genetic analysis”. Furthermore, we have added few statements to motivate the need of genetic analysis and how the webapp can facilitate this (which is introduced in the section 2.6)    

(9) Minor corrections:

(a) Bottom of first page, "always been behavior quantification task" missing "a".

(b) "Type" column in Table S2 is undocumented and unused (i.e., all values are the same); consider removing.

(c) Figure 4B, x-axis: add units.

(d) Page 8/9: all panel references to Figure S1 are off by one

We have fixed them in the updated manuscript.

eLife Assessment

In this important study, the authors conducted extensive atomistic and coarse-grained simulations as well as a lattice Monte Carlo analysis to probe the driving force and functional impact of supercomplex formation in the inner mitochondrial membrane. The study highlighted the major contribution from membrane mechanics to the supercomplex formation and revealed interesting differences in structural and dynamical features of the protein components upon complex formation. Upon revision, the analysis is considered solid, although the magnitude of estimated membrane deformation energies seem somewhat large. Overall, the study is thorough, creative and the impact on the field of bioenergetics is expected to be significant.

Reviewer #1 (Public review):

This paper by Poverlein et al reports the substantial membrane deformation around the oxidative phosphorylation super complex, proposing that this deformation is a key part of super complex formation. I found the paper interesting and well-written.

* Analysis of the bilayer curvature is challenging on the fine lengthscales they have used and produces unexpectedly large energies (Table 1). Additionally, the authors use the mean curvature (Eq. S5) as input to the (uncited, but it seems clear that this is Helfrich) Helfrich Hamiltonian (Eq. S7). If an errant factor of one half has been included with curvature, this would quarter the curvature energy compared to the real energy, due to the squared curvature. The bending modulus used (ca. 5 kcal/mol) is small on the scale of typically observed biological bending moduli. This suggests the curvature energies are indeed much higher even than the high values reported. Some of this may be due to the spontaneous curvature of the lipids and perhaps the effect of the protein modifying the nearby lipids properties.

* It is unclear how CDL is supporting SC formation if its effect stabilizing the membrane deformation is strong or if it is acting as an electrostatic glue. While this is a weakness for a definite quantification of the effect of CDL on SC formation, the study presents an interesting observation of CDL redistribution and could be an interesting topic for future work.

In summary, the qualitative data presented are interesting (especially the combination of molecular modeling with simpler Monte Carlo modeling aiding broader interpretation of the results). The energies of the membrane deformations are quite large. This might reflect the roles of specific lipids stabilizing those deformations, or the inherent difficulty in characterizing nanometer-scale curvature.

Reviewer #3 (Public review):

Summary:

In this contribution, the authors report atomistic, coarse-grained and lattice simulations to analyze the mechanism of supercomplex (SC) formation in mitochondria. The results highlight the importance of membrane deformation as one of the major driving forces for the SC formation, which is not entirely surprising given prior work on membrane protein assembly, but certainly of major mechanistic significance for the specific systems of interest.

Strengths:

The combination of complementary approaches, including an interesting (re)analysis of cryo-EM data, is particularly powerful, and might be applicable to the analysis of related systems. The calculations also revealed that SC formation has interesting impacts on the structural and dynamical (motional correlation) properties of the individual protein components, suggesting further functional relevance of SC formation. In the revision, the authors further clarified and quantified their analysis of membrane responses, leading to further insights into membrane contributions. They have also toned down the decomposition of membrane contributions into enthalpic and entropic contributions, which is difficult to do. Overall, the study is rather thorough, highly creative and the impact on the field is expected to be significant.

Weaknesses:

Upon revision, I believe the weakness identified in previous work has been largely alleviated.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

This paper by Poverlein et al reports the substantial membrane deformation around the oxidative phosphorylation super complex, proposing that this deformation is a key part of super complex formation. I found the paper interesting and well-written.

We thank the Reviewer for finding our work interesting. 

Analysis of the bilayer curvature is challenging on the fine lengthscales they have used and produces unexpectedly large energies (Table 1). Additionally, the authors use the mean curvature (Eq. S5) as input to the (uncited, but it seems clear that this is Helfrich) Helfrich Hamiltonian (Eq. S7). If an errant factor of one half has been included with curvature, this would quarter the curvature energy compared to the real energy, due to the squared curvature.

We thank the Reviewer for raising this important issue. We have now clarified in the SI and main manuscript that we employ the Helfrich model. In our initial implementation, we indeed used the mean curvature H, thereby missing a factor of 2. As the Reviewer correctly noted, this resulted in curvature deformation energies that were underestimated by a factor of ~4. We have now corrected for this effect in the revised analysis, and the updated Table 1. Importantly, however, this correction does not alter the general conclusions of our work that supercomplex formation relieves membrane strain and stabilizes the system. We have added an additional paragraph where we discuss the magnitude of the observed bending effects, and compared the previous estimates in literature:

SI: 

“The local mean curvature of the membrane midplane was computed using the Helfrich model (4,5) …”

(4) W. Helfrich, Elastic properties of lipid bilayers theory and possible experiments. Zeitschrift für Naturforschung 28c, 693-703 (1973).

(5) F. Campelo et al., Helfrich model of membrane bending: From Gibbs theory of liquid interfaces to membranes as thick anisotropic elastic layers. Advances in Colloid and Interface Science 208, 25-33 (2014).

Main Text: 

“which measures the energetic cost of deforming the membrane from a flat geometry (ΔG_curv) based on the Helfrich model (45, 46). …

Our analysis suggests that both contributions are substantially reduced upon formation of the SC, with the curvature penalty decreasing by 79.2 ± 5.2 kcal mol^-1 (for a membrane area of ca. 1000 nm²) and the thickness penalty by 2.8 ± 2.0 kcal mol^-1 (Table 1).”

“We note that the magnitude of the estimated bending energies (~10² kcal mol^-1) (Table 1), while seemingly high at first glance, falls within the range expected for large-scale membrane deformation processes induced by large multi-domain proteins. For example, the Piezo mechanosensitive channel performs roughly 150k_BT (≈ 90 kcal mol⁻¹) of work to bend the bilayer into its dome-like shape (65). Comparable energies have also been estimated for the nucleation of small membrane pores (66), while vesicle formation typically requires bending energies on the order of 300 kcal mol^-1, largely independent of vesicle size (67). When normalized by the affected membrane area (~1000 nm²), these values correspond to an energy density of approximately 0.1 kcal mol^-1 nm^-2, which places our estimates within a biophysically reasonable regime. Notably, cryo-EM structures of several supercomplexes shows that such assemblies can impose significant curvature on the surrounding bilayer (36, 50, 68), supporting the notion that respiratory chain organization is closely coupled to local membrane deformation. Nevertheless, we expect that the absolute deformation energies may be overestimated, as the continuum Helfrich model neglects molecular-level effects such as lipid tilt and local rearrangements, which can partially relax curvature stresses and reduce the effective bending penalty near protein–membrane interfaces (69, 70).”

The bending modulus used (ca. 5 kcal/mol) is small on the scale of typically observed biological bending moduli. This suggests the curvature energies are indeed much higher even than the high values reported. Some of this may be due to the spontaneous curvature of the lipids and perhaps the effect of the protein modifying the nearby lipids properties.

The SI initially included an incorrect value for the bending modulus (20 kJ mol^-1 instead of 20k_BT), which has now been corrected. The revised value is consistent with experimentally reported bending moduli from X-ray scattering measurements, although there remains substantial uncertainty in the precise values across different experimental and computational studies.

“The bending deformation energy was computed from the mean curvature field H(x,y), assuming a constant bilayer bending modulus κ (taken as 20k_bT  = 11.85 kcal mol^-1 (6)):”

(6) S. Brown et al., Comparative analysis of bending moduli in one-component membranes via coarsegrained molecular dynamics simulations. Biophysical Journal 124, 1–13 (2025).

It is unclear how CDL is supporting SC formation if its effect stabilizing the membrane deformation is strong or if it is acting as an electrostatic glue. While this is a weakenss for a definite quantification of the effect of CDL on SC formation, the study presents an interesting observation of CDL redistribution and could be an interesting topic for future work.

We agree with the Reviewer that future studies would be important to investigate the relationship between CDL-induced stabilization of membrane and its electrostatic effects.  

In summary, the qualitative data presented are interesting (especially the combination of molecular modeling with simpler Monte Carlo modeling aiding broader interpretation of the results). The energies of the membrane deformations are quite large. This might reflect the roles of specific lipids stabilizing those deformations, or the inherent difficulty in characterizing nanometer-scale curvature.

We thank the Reviewer for appreciating our work and for the help in further improving our findings.

Reviewer #3 (Public review):

Summary:

In this contribution, the authors report atomistic, coarse-grained and lattice simulations to analyze the mechanism of supercomplex (SC) formation in mitochondria. The results highlight the importance of membrane deformation as one of the major driving forces for the SC formation, which is not entirely surprising given prior work on membrane protein assembly, but certainly of major mechanistic significance for the specific systems of interest.

We thank Reviewer 3 for appreciating the importance of our study. 

Strengths:

The combination of complementary approaches, including an interesting (re)analysis of cryo-EM data, is particularly powerful, and might be applicable to the analysis of related systems. The calculations also revealed that SC formation has interesting impacts on the structural and dynamical (motional correlation) properties of the individual protein components, suggesting further functional relevance of SC formation. In the revision, the authors further clarified and quantified their analysis of membrane responses, leading to further insights into membrane contributions. They have also toned down the decomposition of membrane contributions into enthalpic and entropic contributions, which is difficult to do. Overall, the study is rather thorough, highly creative and the impact on the field is expected to be significant.

Weaknesses:

Upon revision, I believe the weakness identified in previous work has been largely alleviated.

We thank the Reviewer for their previous remarks, which allowed us to significantly improve our manuscript.

eLife Assessment

This study provides important findings on the understanding of circannual timing in mammals, for which iodothyronine deiodinases (DIOs) have been suggested to be of critical importance, yet functional genetic evidence has been missing. The authors convincingly implicate dio3, the major inactivator of the biologically active thyroid hormone T3, in circannual timing in Djungarian hamsters, using a combination of correlative and gene knock-out experiments; thus this provides key insights into the evolution and function of animal annual timing mechanisms.

Reviewer #1 (Public review):

Circannual timing is a phylogenetically widespread phenomenon in long-lived organisms and is central to the seasonal regulation of reproduction, hibernation, migration, fur color changes, body weight, and fat deposition in response to photoperiodic changes. Photoperiodic control of thyroid hormone T3 levels in the hypothalamus dictates this timing. However, the mechanisms that regulate these changes are not fully understood. The study by Stewart et al. reports that hypothalamic iodothyronine deiodinase 3 (Dio3), the major inactivator of the biologically active thyroid hormone T3, plays a critical role in circannual timing in the Djungarian hamster. Overall, the study yields important results for the field and is well-conducted, with the exception of the CRISPR/Cas9 manipulation.

Comments on revisions:

The authors have satisfactorily addressed all my comments. I no longer have concerns about the CRISPR/Cas9 experiments which have been conducted properly and are now reported appropriately.

Reviewer #2 (Public review):

Summary:

Several animals and plants adjust their physiology and behavior to seasons. These changes are timed to precede the seasonal transitions, maximizing chances of survival and reproduction. The molecular mechanisms used for this process are still unclear. Studies in mammals and birds have shown that the expression of deiodinase type-1, 2, and 3 (Dio1, 2, 3) in the hypothalamus spikes right before the transition to winter phenotypes. Yet, whether this change is required or an unrelated product of the seasonal changes has not been shown, particularly because of the genetic intractability of the animal models used to study seasonality. Here, the authors show for the first time a direct link between Dio3 expression and the modulation of circannual rhythms.

The work is concise and presents the data in a clear manner. The data is, for the most part, solid and supports the author's main claims. The use of CRISPR is a clear advancement in the field. This is, to my knowledge, the first study showing a clear (i.e., causal) role of Dio3 in the circannual rhythms in mammals. Having established a clear component of the circannual timing and a clean approach to address causality, this study could serve as a blueprint to decipher other components of the timing mechanism. It could also help to enlighten the elusive nature of the upstream regulators, in particular, on how the integration of day length takes place, maybe within the components in the Pars tuberalis, and the regulation of tanycytes.

Comments on revisions:

The authors have provided an improved version of the manuscript, particularly clarifying the methodology for their CRISPR manipulations. I am satisfied with their response and commend the authors for their work.

Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public review):

Circannual timing is a phylogenetically widespread phenomenon in long-lived organisms and is central to the seasonal regulation of reproduction, hibernation, migration, fur color changes, body weight, and fat deposition in response to photoperiodic changes. Photoperiodic control of thyroid hormone T3 levels in the hypothalamus dictates this timing. However, the mechanisms that regulate these changes are not fully understood. The study by Stewart et al. reports that hypothalamic iodothyronine deiodinase 3 (Dio3), the major inactivator of the biologically active thyroid hormone T3, plays a critical role in circannual timing in the Djungarian hamster. Overall, the study yields important results for the field and is well-conducted, with the exception of the CRISPR/Cas9 manipulation.

We appreciate the positive and supportive comment from the Reviewer. We have clarified the oversight in the Crispr/Cas9 data representation below. Our correction should alleviate any concern raised.

Figure 1 lays the foundation for examining circannual timing by establishing the timing of induction, maintenance, and recovery phases of the circannual timer upon exposure of hamsters to short photoperiod (SP) by monitoring morphological and physiological markers. Measures of pelage color, torpor, body mass, plasma glucose, etc, established that the initiation phase occurred by weeks 4-8 in SP, the maintenance by weeks 12-20, and the recovery after week 20, where all morphological and physiological changes started to reverse back to long photoperiod phenotypes.

The statistical analyses look fine, and the results are unambiguous.

We thank the Reviewer for recognizing our attempts to highlight the phenomenon of circannual interval timing.

Their representation could, however, be improved. In Figures 1d and 1e, two different measures are plotted on each graph and differentiated by dots and upward or downward arrowheads. The plots are so small, though, that distinguishing between the direction of the arrows is difficult. Some color coding would make it more reader-friendly. The same comment applies to Figure S4. 

We have increased the panel size for Figure 1d and 1e. We have also changed the colour of the graphs in Figure 1d and 1e to facilitate the differentiation of the two dependent variables. For the circos plots, we attempted different ways to represent the data. We have opted to keep the figures in their current stage. The overall aim is to provide a ‘gestalt’ view of the timing of changes in transcript expression and highlighted only a few key genes. The whole dataset is provided in the supplementary materials for Reviewer/Reader interrogation.

The authors went on to profile the transcriptome of the mediobasal and dorsomedial hypothalamus, paraventricular nucleus, and pituitary gland (all known to be involved in seasonal timing) every 4 weeks over the different phases of the circannual interval timer. A number of transcripts displaying seasonal rhythms in expression levels in each of the investigated structures were identified, including transcripts whose expression peaks during each phase. This included two genes of particular interest due to their known modulation of expression in response to photoperiod, Dio3 and Sst, found among the transcripts upregulated during the induction and maintenance phases, respectively. The experiments are technically sound and properly analyzed, revealing interesting candidates. Again, my main issues lie with the representation in the figure. In particular, the authors should clarify what the heatmaps on the right of Figures 1f and 1g represent. I suspect they are simply heatmaps of averaged expression of all genes within a defined category, but a description is missing in the legend, as well as a scale for color coding near the figure.

We have clarified the heatmap and density maps in the Figure legend. We apologise for the lack of information to describe the figure panels. (see lines 644-648)

Figure 2 reveals that SP-programmed body mass loss is correlated to increased Dio3-dependent somatostatin (Sst) expression. First, to distinguish whether the body mass loss was controlled by rheostatic mechanisms and not just acute homeostatic changes in energy balance, experiments from hamsters fed ad lib or experiencing an acute food restriction in both LP and SP were tested. Unlike plasma insulin, food restriction had no additional effect on SP-driven epididymal fat mass loss (Figure S7). This clearly establishes a rheostatic control of body mass loss across weeks in SP conditions. Importantly, Sst expression in the mediobasal hypothalamus increased in both ad lib fed or restriction fed SP hamsters and this increase in expression could be reduced by a single subcutaneous injection of active T3, clearly suggesting that increase in Sst expression in SP is due to a decrease of active T3 likely via Dio3 increase in expression in the hypothalamus. The results are unambiguous

We thank the Reviewer for the supportive and affirmative feedback.

Figure 3 provides a functional test of Dio3's role in the circannual timer. Mediobasal hypothalamic injections of CRISPR-Cas9 lentiviral vectors expressing two guide RNAs targeting the hamster Dio3 led to a significant reduction in the interval between induction and recovery phases seen in SP as measured by body mass, and diminished the extent of pelage color change by weeks 15-20. In addition, hamsters that failed to respond to SP exposure by decreasing their body mass also had undetectable Dio3 expression in the mediobasal hypothalamus. Together, these data provide strong evidence that Dio3 functions in the circannual timer. I noted, however, a few problems in the way the CRISPR modification of Dio3 in the mediobasal hypothalamus was reported in Figure S8. One is in Figure S8b, where the PAM sites are reported to be 9bp and 11bp downstream of sgRNA1 and sgRNA2, respectively. Is this really the case? If so, I would have expected the experiment to fail to show any effect as PAM sites need to immediately follow the target genomic sequence recognized by the sgRNA for Cas9 to induce a DNA double-stranded break. It seems that each guide contains a 3' NGG sequence that is currently underlined as part of sgRNAs in both Fig S8b and in the method section. If this is not a mistake in reporting the experimental design, I believe that the design is less than optimal and the efficiencies of sgRNAs are rather low, if at all functional.

We apologize for the oversight and indeed the reporting in Figure S8b was a mistake. The PAM site previously indicated was the ‘secondary PAM site’ (which as the Reviewer notes would likely have low efficiency). The PAM site is described within the gRNA in the figure. We use Adobe Illustrator to generate figures, and during the editing process, the layer for PAM text was accidentally moved ‘back’ to a lower level. The oversight was not rectified before submission. We apologise for this unreservedly. The PAM site text has been moved forward, to highlight the location of the primary site (ie immediately following gRNA) and labelled the gRNA and PAM site in the ‘Target region’. The secondary PAM site text was removed to eliminate any confusion.

The authors report efficiencies around 60% (line 325), but how these were obtained is not specified. 

The efficiency provided are based on bioinformatic analyses and not in vivo assays. To reduce any confusion, we have removed the text. The gRNA were clearly effective to induce mutations based on the sequencing analyses.

Another unclear point is the degree to which the mediobasal hypothalamus was actually mutated. Only one mutated (truncated) sequence in Figure S8c is reported, but I would have expected a range of mutations in different cells of the tissue of interest.

The tissue punch would include multiple different cells (e.g., neuronal, glial, etc). We agree with the Reviewer that genomic samples from different cells would be included in the sequencing analyses. Given the large mutation in the target region, the gRNA was effective. We have only shown one representative sequence. If the Reviewer would like to see all mutations, we can easily show the other samples.

Although the authors clearly find a phenotypic effect with their CRISPR manipulation, I suspect that they may have uncovered greater effects with better sgRNA design. These points need some clarification. I would also argue that repeating this experiment with properly designed sgRNAs would provide much stronger support for causally linking Dio3 in circannual timing.

The gRNA was designed using the Gold-standard approach – ChopChop [citation Labon et al., 2019]. If the Reviewer’s concern re design is due to the comment above re PAM site; this issue was clarified and there are no concerns for the gRNA design. The major challenge with the Dio3 gene (single exon) with a very short sequence length (approx.. 412bp). There is limited scope within this sequence length to generate gRNA.

A proposed schematic model for mechanisms of circannual interval timing is presented in Figure S9. I think this represents a nice summary of the findings put in a broader context and should be presented as a main figure in the manuscript itself rather than being relayed in supplementary materials.

We agree with the Reviewer position and moved the figure to the main manuscript. The figure is now Figure 4.

Reviewer #2 (Public review):

Several animals and plants adjust their physiology and behavior to seasons. These changes are timed to precede the seasonal transitions, maximizing chances of survival and reproduction. The molecular mechanisms used for this process are still unclear. Studies in mammals and birds have shown that the expression of deiodinase type-1, 2, and 3 (Dio1, 2, 3) in the hypothalamus spikes right before the transition to winter phenotypes. Yet, whether this change is required or an unrelated product of the seasonal changes has not been shown, particularly because of the genetic intractability of the animal models used to study seasonality. Here, the authors show for the first time a direct link between Dio3 expression and the modulation of circannual rhythms.

We appreciate the clear synthesis and support for the manuscript.

Strengths:

The work is concise and presents the data in a clear manner. The data is, for the most part, solid and supports the author's main claims. The use of CRISPR is a clear advancement in the field. This is, to my knowledge, the first study showing a clear (i.e., causal) role of Dio3 in the circannual rhythms in mammals. Having established a clear component of the circannual timing and a clean approach to address causality, this study could serve as a blueprint to decipher other components of the timing mechanism. It could also help to enlighten the elusive nature of the upstream regulators, in particular, on how the integration of day length takes place, maybe within the components in the Pars tuberalis, and the regulation of tanycytes.

We thank the Reviewer for this positive summary.

Weaknesses:

Due to the nature of the CRISPR manipulation, the low N number is a clear weakness. This is compensated by the fact that the phenotypes shown here are strong enough. Also, this is the only causal evidence of Dio3's role; thus, additional evidence would have significantly strengthened the author's claims. The use of the non-responsive population of hamsters also helps, but it falls within the realm of correlations.

We would also like to remind the Reviewer that one Crispr-Cas9 Dio3^cc treated hamster did not show any mutation in the genome. This hamster was observed to have a change in body mass and pelage colour like controls. This animal provides another positive control.

We also conducted a statistical power analysis to examine whether n=3 is sufficient for the Dio3^cc treatment group. Using the appropriate expected difference in means and standard deviations for an alpha of 0.05; we regularly observed beta >0.8 across the dependent variables. 

Additionally, the consequences of the mutations generated by CRISPR are not detailed; it is not clear if the mutations affect the expression of Dio3 or generate a truncation or deletion, resulting in a shorter protein.

We agree with the Reviewer that transcript and protein assays would strengthen the genome mutation data. Due to the small brain region under investigation, we are limited in the amount of biological material to extract. Dio3 is an intronless gene and very short – approximately 412 base pairs in length. We opted to maximize resources into sequencing the gene as the confirmation of genetic mutation is paramount. Given the large size of the mutation in the treated hamsters, there would be no amplification of transcript or protein translated.

Reviewer #3 (Public review):

The authors investigated SP-induced physiological and molecular changes in Djungarian hamsters and the endogenous recovery from it after circa half a year. The study aimed to elucidate the intrinsic mechanism and included nice experiments to distinguish between rheostatic effects on energy state and homeostatic cues driven by an interval timer. It also aimed to elucidate the role of Dio3 by introducing a targeted mutation in the MBH by ICV. The experiments and analyses are sound, and the amount of work is impressive. The impact of this study on the field of seasonal chronobiology is probably high.

We thank the Reviewer for their positive comments and support for our work.

Even though the general conclusions are well-founded, I have fundamental criticism concerning 3 points, which I recommend revising:

(1) The authors talk about a circannual interval timer, but this is no circannual timer. This is a circasemiannual timer. It is important that the authors use precise wording throughout the manuscript.

We agree with the Reviewer that the change in physiology and behaviour does not approximate a full year (e.g. annual) and only a half of the year. We opted to use circannual timer as this term is established in the field (see doi: 10.1177/0748730404266626; doi: 10.1098/rstb.2007.2143). We cannot identify any publication that has used the term ‘semiannual timer’. We do not feel this manuscript is the appropriate time to introduce a new term to the field; we will endeavour to push the field to consider the use of ‘semiannual timer’. A Review or Opinion paper is best place for this discussion. We hope the Reviewer will understand our position.

(2) The authors put their results in the context of clocks. For example, line 180/181 seasonal clock. But they have described and investigated an interval timer. A clock must be able to complete a full cycle endogenously (and ideally repeatedly) and not only half of it. In contrast, a timer steers a duration. Thus, it is well possible that a circannual clock mechanism and this circa-semiannual timer of photoperiodic species are 2 completely different mechanisms. The argumentation should be changed accordingly.

We agree with the Reviewers definitions of circannual ‘clock’ and ‘timer’. We were careful to distinguish between the two concepts early in the manuscript (lines 41-46). We have added italics to emphasis the different terms. The use of seasonal clock on line 180/191 was imprecise and we appreciate the Reviewer highlighting our oversight and the text was revised. We have also revised the Abstract accordingly.

(3) The authors chose as animal model the Djungarian hamster, which is a predominantly photoperiodic species and not a circannual species. A photoperiodic species has no circannual clock. That is another reason why it is difficult to draw conclusions from the experiment for circannual clocks. However, the Djungarian hamster is kind of "indifferent" concerning its seasonal timing, since a small fraction of them are indeed able to cycle (Anchordoquy HC, Lynch GR (2000), Evidence of an annual rhythm in a small proportion of Siberian hamsters exposed to chronic short days. J Biol Rhythms 15:122-125.). Nevertheless, the proportion is too small to suggest that the findings in the current study might reflect part of the circannual timing. Therefore, the authors should make a clear distinction between timers and clocks, as well as between circa-annual and circa-semiannual durations/periods.

This comment is not clear to us. The Reviewer states the hamsters are not a circannual species, but then highlight one study that shows circannual rhythmicity. We agree that circannual rhythmicity in Djungarian hamsters is dependent on the physiological process under investigation (e.g. body mass versus reproduction) and that photoperiodic response system either dampen or mask robust cycles. We have corrected the text oversight highlighted above and the manuscript is focused on interval timers. We have kept the term circannual over semicircannual due to the prior use in the scientific literature.

Reviewing Editor Comments:

The detailed suggestions of the reviewers are outlined below (or above in case of reviewer 1). In light of the criticism, we ask the authors to especially pay attention to the comments on the Cas9/Crisp experiment, raised by Reviewers 1 and 2. As currently described, there are serious questions on the design of the sgRNAs, and also missing critical methodological details. If the latter are diligently taken care of, they may resolve the questions on the sgRNA design. Please also reconsider the wording along the suggestions of Reviewer 3.

We appreciate the Editors time and support for the manuscript. We have clarified and corrected our oversight for the PAM site. This correction confirms the strength of the Crispr-cas9 gRNA used in the study. The correction should remove all concerns. We have also considered using semicircannual in the text. As there is existing scientific literature using circannual interval timer, and there is no publication to our knowledge for using ‘semicircannual; we have opted to keep with the current approach and use circannual. We feel a subsequent Opinion paper is more suitable to introduce a new term.

Reviewer #2 (Recommendations for the authors):

First, I want to commend the authors for their work. It is a clear advancement for our field. Below are a couple of comments and suggestions I have:

we thank the Review for the positive comment and support. We have endeavoured to incorporate their suggested improvements to the manuscript.

(1) Looking at the results of Figure 1A and Figure S8, the control in S8 showed a lower pelage color score as compared to the hamsters in 1A. Is this a byproduct of the ICV injection?

The difference between Figure 1 and 3 is likely due to the smaller sample sizes. The controls in Figure 1 had a higher proportion of hamsters show complete white fur (score =3) at 1618 weeks compared to controls in Figure 3. It is possible, although unlikely that the ICV injection would reduce the development of winter phenotype. There was no substance in the ICV injection that would impact the prolactin signalling pathway. Our perspective is that the difference between the two figures is due to the different sampling population. Overall, the timing of the change in pelage colour is the same between the figures and suggest that the mechanisms of interval timer were unaffected.

(2) Is there a particular reason why the pelage color for the CRISPR mutants is relegated to the supplemental information? In my opinion, this is also important, even though the results might be difficult to explain. Additionally, did the authors check for food intake and adipose mass in these animals?

We agree with the Reviewer the pelage change is very interesting. We decided to have Figure 3 focus on body mass. The rationale was due to the robust nature of the data collection from Crispr-cas9 study (Fig.3b), in addition to the non-responsive hamsters (Fig.3e). We disagree that the data patterns are hard to explain, as pelage changes was similar to the photoperiodic induced change in body mass. No differences were observed for food intake or adipose tissue. We have added this information in the text (see lines 162-163).

(3) I might have missed it, but did the authors check for the expression of Dio3 on the CRISPR mutants? Does the deletion cause reduced expression or any other mRNA effect, such as those resulting in the truncation of a protein?

Due to the limited biological material extracted from the anatomical punches, we decided to focus on genomic mutations. Dio3 has a very short sequence length and the size of the mutations identified indicate that no RNA could be transcribed.

(4) Could the authors clarify which reference genome or partial CDS (i.e., accession numbers) they used to align the gRNA? Did they use the SSSS strain or the Psun_Stras_1 isolate?

The gRNAs were designed using the online tool CHOPCHOP, using the Mus musculus

Dio3 gene. The generated gRNAs were subsequently aligned via blast with the Phodopus sungorus Dio3 partial cds (GenBank: MF662622.1), to ensure alignment with the species. We are confident that the gRNA designed align 100% in hamsters. Furthermore, we conducted BLAST to ensure there were no off-targets. The only gene identified in the BLAST was the rodent (i.e. hamster, mouse) Dio3 sequence.

(5) Figure 3b. I do agree with the authors in pointing out that the decrease in body mass is occurring earlier in Dio3wt hamsters; however, the shape of the body mass dynamic is also different. Do the authors have any comments on the possible role of Dio3 in the process of exist of overwintering?

This is a very interesting question. We do not have the data to evaluate the role of Dio3 for overwintering. We argue that disruption in Dio3 reduced the circannual interval period. For this interpretation, yes, Dio3 is necessary for overwintering. However, we would need to show the sufficiency of Dio3 to induce the winter phenotype in hamsters housed in long photoperiod. At this time, we do not have the technical ability to conduct this experiment.

(6) In Figure 3d, the Dio3wt group does not show any dispersion. Is this correct? If that's true, and no dispersion is observed, no normality can be assumed, and a t-test can't be performed (Line 692).The Mann-Whitney test might be better suited.

We conducted a Welch’s t-test to compare the difference in body mass period. We used the Welch’s test as the variance were not equal; Mann-Whitney test is best for skewed distributions. To clarify the test used, we have added ‘Welch’s test’ to the Figure legend.

(9) Figure 1 h. It might be convenient to add the words "Induction", "maintenance", and "recovery" over each respective line on the polar graph for easier reading.

We have added the text as suggested by the Reviewer.

Reviewer #3 (Recommendations for the authors):

(1) Figure 1: Please enlarge all partial graphics at least to the size of Figure 2. In the print version, labels are barely readable

we have increased the panels in Figure 1 and 3 by 20% to accommodate the Reviewers suggestion.

(2) Legend Figure 2: Add that the food restriction was 16h.

We have added 16h to the text.

(3) Figure 3b: enlarge font size. In the legend: Dio3cc hamsters delayed.... The delay might have been a week or so, but not more (and even that is unclear since the rise in body mass in that week seems to be rather a disturbance of the curve). Thus 'delay' might not be the most appropriate wording. Instead, the initial decline is slower, but both started at nearly the same week (=> no delay). Minimum body mass is reached at the identical week as in wt (=> no delay). Also, the increase started at the same week but was much faster in Dio3cc than in wt. Figure 3c: How can there be a period when there is no repeated cycle (rhythm)? This is rather a duration. Moreover, according to the displayed data, I am wondering which start point and which endpoint is used. The first and last values are the highest of the graph, but have they been the maximum? Especially for Dio3wt, it can be assumed that animals haven't reached the maximum at the end of the graph.

We have increased the font size in Figure 3b. We have changed ‘delayed’ to ‘slower’ in the text. Period analyses, such as the Lomb-Scargle measure the duration of a cycle (and multiple cycles). The start point and end point used in the analyses were the initial data collection date (week 0) and the final data collection date (week 32). The Lomb-Scargle analyses determines the duration of the period that occurs within these phases of the cycle. We believe the period analyses conducted by the Lomb-Scargle is the most suitable for the scientific question.

(4) Figure S9: This is a very nice graph and summarises your main results. It should appear in the main manuscript and not in the supplements.

We appreciate the positive comment and suggestion. We agree with the Reviewer and have move the graph to the main figure. The revised manuscript indicates the graph as Figure 4.

eLife Assessment

The results in this study are useful because they begin to establish a causal link between physical activity and the cellular mechanisms of regeneration. The evidence presented is largely solid, supporting the conclusion that exercise-induced changes in the extracellular matrix disrupt regeneration; however, some claims are incomplete, requiring additional controls and a clearer distinction between the effects of mechanical loading and mechanical injury to the blastema. The work will be of interest to researchers in regenerative medicine.

Reviewer #1 (Public review):

Summary:

The goal of the manuscript was to determine if strenuous exercise negatively impacted regeneration. Indeed, the major conclusion of the manuscript is that elevated exercise during the early stages of regeneration compromises the regenerative process. The authors further conclude that regeneration is disrupted due to defects in blastema formation, which is caused by impaired HA deposition and reduced active (nuclear) Yap.

Strengths:

(1) The paradigm of elevated exercise disrupting ECM and regeneration is significant, and provides an experimental model to better understand connections between the ECM and cell/tissue activities.

(2) The conclusion that exercise intensity correlates with defects in regeneration is supported.

(3) The demonstration for the requirement for HA is well supported via transcriptomics and multiple independent strategies to manipulate HA levels.

(4) The demonstration that nuclear Yap depends on the amount of HA is well-supported.

Weaknesses:

(1) The authors conclude throughout the manuscript that "blastema formation" is disrupted, but they do not provide any insights into how blastema formation is disrupted (reduced de-differentiation? reduced cell migration? both?). While they show that there are fewer dividing cells, the timing of exercise is prior to outgrowth. So, the effect of dividing cells is likely secondary, which is not considered (or not clearly explained).

(2) The authors conclude that patterning is affected, but their analyses of patterns (bifurcations) are very limited. It is also not clear if patterning is believed to be affected by a common exercise-induced mechanism or a different exercise-induced mechanism (or by a secondary mechanism).

(3) The significance of HA in regeneration has been shown before in zebrafish fins, as well as in a handful of other models of regeneration. Although largely cited, explaining some of this work in more detail would give the reader a better picture of how HA is believed to promote regeneration. It may also highlight some emerging questions about the role of HA in regeneration that would permit a richer story and specific future directions.

(4) In general, parts of the text lack specificity/clarity, and in other cases, there seems to be contradictory information.

(5) Overall, many of the conclusions were well supported by the data, and this study is likely to provide a foundation for future research on the role of the ECM in tissue repair and regeneration. The main limitations were in connecting the experimental details with the specific processes required for regeneration, and in clearly explaining the findings.

Reviewer #2 (Public review):

In this study, Lewis et al. established a forced swimming paradigm to investigate how mechanical loading influences caudal fin regeneration. They found that forced exercise impaired the normally robust regeneration process, particularly in the peripheral/lateral ray regions. Transcriptomic profiling of exercised fish further revealed that extracellular matrix (ECM) gene programs were affected, and the authors provided evidence that disruption of hyaluronic acid (HA) synthesis may underlie this impairment. While the question of how mechanical loading impacts tissue regeneration is rather intriguing and the study nicely demonstrates a role for HA in fin regeneration, I have some concerns regarding the specificity of forced exercise as a model for mechanical loading, and thus the causal link between mechanical loading and HA synthesis disruption.

Major concerns:

(1) Forced exercise as a model for mechanical loading.

Is it possible that the forced exercise paradigm imposes greater shear stress on the peripheral/lateral ray regions, thereby disrupting the fragile wound epidermis at this early stage and consequently affecting the regeneration program and phenotypes? The wound epidermis appears visibly torn or disrupted (Figure 1A, right panel, 2 dpa image). Given the critical role of the wound epidermis in blastema establishment and fin regeneration (PMID: 11002347; PMID: 34038742; PMID: 26305099), could this be a simpler explanation to consider, instead of the proposed role of mechanical loading and cryptic mechanical sensors?

(2) The general effect of HA on fin regeneration.

While the authors convincingly show that exogenous HA can ameliorate fin regeneration defects caused by forced exercise (Figure S7), it would be important to include a control examining the effect of HA supplementation in non-exercised animals. Does HA act as a general enhancer of fin regeneration even in the absence of forced exercise? Additionally, please consider merging Figure S7 (HA supplement) with Figure 5 (HA depletion) to improve clarity for readers.

(3) Proper annotation of the investigated ray regions.

As the authors clearly demonstrate that peripheral and central rays respond differently to forced exercise, it is important to explicitly define the regions corresponding to these rays. Do the peripheral rays refer to the dorsal-most and ventral-most rays among the 18-20 rays across the amputation plane? Which rays are considered central? Please clarify.

Reviewer #3 (Public review):

Summary:

In the submitted article by Lewis et al., the authors investigate how mechanical stimulation influences organ regeneration using the well-characterized zebrafish caudal fin regeneration model. Using a swim flume and a 30min/day exercise regime, the authors found that exercise during the establishment of the blastema reduced regeneration and led to skeletal deformations. Transcriptional profiling of regenerated caudal fin tissue revealed reduced expression of extracellular matrix-associated genes, which were found to be expressed by blastemal fibroblast and osteoblast lineage cells.

Downregulated genes included hyaluronic acid synthases 1 and 2; accordingly, hyaluronic acid levels were found to be reduced in regenerating fins exposed to exercise. The link between regeneration and HA was further confirmed through HA depletion and HA overexpression experiments, which showed a reduction in blastema size and partial rescue of blastema formation, respectively. The authors further show that HA levels, as well as the extent of mechanical loading correlate with nuclear localization of the mechanotransducer Yap and conclude that biomechanical forces play a significant role during regeneration through regulation of HA levels in the ECM and therewith regulation of YAP downstream signaling.

This work expands our understanding of the biochemical signaling connecting biomechanical forces with tissue regeneration. The conclusions are well supported by the data.

Strengths:

(1) Analysis is performed in multiple replicate experimental groups and shows the robust response to the experimental conditions.

(2) The link of HA levels to blastema formation was confirmed through HA overexpression and two different HA depletion experiments.

(3) The use of a previously established fin regeneration single cell dataset does elegantly show the correlation of changes in gene expression levels and specific tissue types, which was further confirmed by in vivo imaging of cell type-specific transgenic lines.

Weaknesses:

Tissue sections stained with hematoxylin and eosin would be helpful to show the changes in tissue architecture more clearly.

Author response:

Reviewer #1

We agree that further clarification how elevated exercise disrupts blastema formation would strengthen the manuscript. Our data suggests a major contribution of proliferation. Exercise reduced the fraction of proliferative cells at 3 dpa, consistent with disrupted HA production and downstream Yap signaling. This interpretation aligns with prior studies showing that proliferation contributes to blastema establishment and is not restricted to the outgrowth phase of fin regeneration (Poleo et al, 2001; Poss et al, 2002; Wang et al, 2019; Pfefferli et al, 2014; Hou et al, 2020). We will explore additional experiments to reinforce these insights into the cellular mechanisms underlying exercise-disrupted blastema formation.

We acknowledge that our analysis of ray branching abnormalities is limited in the current manuscript. We focus our study on introducing the zebrafish swimming and regeneration model and then characterizing ECM and signaling changes accounting for disrupted blastema establishment. For completeness, we included the observation of skeletal patterning defects (branching delays and bone fusions) but without detailed analysis. We note that decreased expression of shha and Shh-pathway components following early exercise corresponds with the branching defects. However, we recognize exercise could have additional effects during the outgrowth  phase when branching morphogenesis actively occurs. Therefore, we will expand our discussion to outline future research directions related to exercise impacts on regenerative skeletal patterning.

We will expand the Introduction and/or Discussion sections to provide more context on known HA roles across regeneration contexts, including in zebrafish fins. Finally, we will improve the text’s clarity and specificity throughout the manuscript, including to resolve or explain any apparent contradictions.

Reviewer #2

We appreciate the Reviewer's concern regarding the specificity of forced exercise as a model for mechanical loading. Forced exercise has been widely used in vivo to induce mechanical loading without the requirement for specialized implants or animal restraint, including in mouse (Wallace et al, 2015; Bomer et al, 2016), rat (Honda et al, 2003; Boerckel et al, 2011; Boerckel et al, 2012), and, most relevant to our study, zebrafish models (Fiaz et al, 2012; Fiaz et al, 2014; Suniaga et al, 2018). However, we will expand our discussion of this approach and ensure precise language distinguishing exercise from mechanical loading.

We acknowledge the possibility that early shear stress disrupts the wound epidermis, which we will elaborate on in a revised Discussion. However, exercise-induced disruptions to the fin epidermis of early regenerates (1–2 dpa; Figure 2) typically resolve within one day, whereas fibroblast lineage cells still fail to establish a robust blastema. Therefore, sustained effects of mechanical loading and/or mechanosensation are likely major contributors to the observed regeneration phenotypes.

We will explore whether HA acts as a general enhancer of fin regeneration by comparing blastemal HA supplementation vs. controls in non-exercised regenerating animals, if technically feasible. We will merge Figure S7 (HA supplementation) with Figure 5 (HA depletion) for clarity, as suggested.

We will include a schematic and clear definitions for 'peripheral' and 'central' rays in a revised manuscript.

Reviewer #3

We included Hoechst and eosin fluorescent staining in the manuscript to show changes in tissue architecture following swimming exercise (Supplemental Figure 4). We will extend this histological analysis to include hematoxylin and eosin staining to provide additional tissue visualization.

References

Poleo G, Brown CW, Laforest L, Akimenko MA. Cell proliferation and movement during early fin regeneration in zebrafish. Dev Dyn. 2001 Aug;221(4):380-90.

Poss KD, Nechiporuk A, Hillam AM, Johnson SL, Keating MT. Mps1 defines a proximal blastemal proliferative compartment essential for zebrafish fin regeneration. Development. 2002 Nov;129(22):5141-9.

Wang YT, Tseng TL, Kuo YC, Yu JK, Su YH, Poss KD, Chen CH. Genetic Reprogramming of Positional Memory in a Regenerating Appendage. Curr Biol. 2019 Dec 16;29(24):4193-4207.e4.

Pfefferli C, Müller F, Jaźwińska A, Wicky C. Specific NuRD components are required for fin regeneration in zebrafish. BMC Biol. 2014 Apr 29;12:30.

Hou Y, Lee HJ, Chen Y, Ge J, Osman FOI, McAdow AR, Mokalled MH, Johnson SL, Zhao G, Wang T. Cellular diversity of the regenerating caudal fin. Sci Adv. 2020 Aug 12;6(33):eaba2084.

Wallace IJ, Judex S, Demes B. Effects of load-bearing exercise on skeletal structure and mechanics differ between outbred populations of mice. Bone. 2015 Mar;72:1-8.

Bomer N, Cornelis FM, Ramos YF, den Hollander W, Storms L, van der Breggen R, Lakenberg N, Slagboom PE, Meulenbelt I, Lories RJ. The effect of forced exercise on knee joints in Dio2(-/-) mice: type II iodothyronine deiodinase-deficient mice are less prone to develop OA-like cartilage damage upon excessive mechanical stress. Ann Rheum Dis. 2016 Mar;75(3):571-7.

Honda A, Sogo N, Nagasawa S, Shimizu T, Umemura Y. High-impact exercise strengthens bone in osteopenic ovariectomized rats with the same outcome as Sham rats. J Appl Physiol (1985). 2003 Sep;95(3):1032-7.

Boerckel JD, Kolambkar YM, Stevens HY, Lin AS, Dupont KM, Guldberg RE. Effects of in vivo mechanical loading on large bone defect regeneration. J Orthop Res. 2012 Jul;30(7):1067-75.

Boerckel JD, Uhrig BA, Willett NJ, Huebsch N, Guldberg RE. Mechanical regulation of vascular growth and tissue regeneration in vivo. Proc Natl Acad Sci U S A. 2011 Sep 13;108(37):E674-80.

Fiaz AW, Léon-Kloosterziel KM, Gort G, Schulte-Merker S, van Leeuwen JL, Kranenbarg S. Swim-training changes the spatio-temporal dynamics of skeletogenesis in zebrafish larvae (Danio rerio). PLoS One. 2012;7(4):e34072.

Fiaz AW, Léon‐Kloosterziel KM, van Leeuwen JL, Kranenbarg S. Exploring the molecular link between swim‐training and caudal fin development in zebrafish (Danio rerio) larvae. Journal of Applied Ichthyology. 2014 Aug;30(4):753-61.

Suniaga S, Rolvien T, Vom Scheidt A, Fiedler IAK, Bale HA, Huysseune A, Witten PE, Amling M, Busse B. Increased mechanical loading through controlled swimming exercise induces bone formation and mineralization in adult zebrafish. Sci Rep. 2018 Feb 26;8(1):3646.

eLife Assessment

This important work characterizes layers of neuropeptidergic modulations that collectively regulate the intake of sugar in a hunger state-dependent manner. Combinations of genetic, physiological, and behavioral approaches present convincing evidence that neurons that release Hugin and Allatostatin A are in an active state in sated flies, leading to suppression of sugar feeding behavior by reducing the sensitivity of sugar-sensitive gustatory neurons that express Gr5a. They also demonstrate that neurons that release Neuromedin U, a vertebrate homolog of Hugin, have common physiological properties as the fly Hugin neurons, revealing a similar function of evolutionarily conserved peptides across animal phyla.

Reviewer #1 (Public review):

In this manuscript, Qin and colleagues aim to delineate a neural mechanism by which the internal satiety levels modulate the intake of sugar solution. They identified a three-step neuropeptidergic system that downregulates the sensitivity of sweet-sensing gustatory sensory neurons in sated flies. First, neurons that release a neuropeptide Hugin (which is an insect homolog of vertebrate Neuromedin U (NMU)) are in an active state when the concentration of glucose is high. This activation does not require synaptic inputs, suggesting that Hugin-releasing neurons sense hemolymph glucose levels directly. Next, the Hugin neuropeptides activate Allatostatin A (AstA)-releasing neurons via one of Hugin's receptors, PK2-R1. Finally, the released AstA neuropeptide suppresses sugar response in sugar-sensing Gr5a-expressing gustatory sensory neurons through AstA-R1 receptor. Suppression of sugar response in Gr5a-expressing neurons reduces the fly's sugar intake motivation (measured by proboscis extension reflex). They also found that NMU-expressing neurons in the ventromedial hypothalamus (VMH) of mice (which project to the rostral nucleus of the solitary tract (rNST)) are also activated by high concentrations of glucose, independent of synaptic transmission, and that injection of NMU reduces the glucose-induced activity in the downstream of NMU-expressing neurons in rNST. These data suggest that the function of Hugin neuropeptide in the fly is analogous to the function of NMU in the mouse.

Generally, their central conclusions are well-supported by multiple independent approaches. The parallel study in mice adds a unique comparative perspective that makes the paper interesting to a wide range of readers. It is easier said than done: the rigor of this study, which effectively combined pharmacological and genetic approaches to provide multiple lines of behavioral and physiological evidence, deserves recognition and praise.

A perceived weakness is that the behavioral effects of the manipulations of Hugin and AstA systems are modest compared to a dramatic shift of sugar solution-induced PER (the behavioral proxy of sugar sensitivity) induced by hunger, as presented in Figure 1B and E. It is true that the mutation of tyrosine hydroxylase (TH), which synthesizes dopamine, does not completely abolish the hunger-induced PER change, but the remaining effect is small. Moreover, the behavioral effect of the silencing of the Hugin/AstA system (Figure Supplement 13B, C) is difficult to interpret, leaving a possibility that this system may not be necessary for shifting PER in starved flies. These suggest that the Hugin-AstA system accounts for only a minor part of the behavioral adaptation induced by the decreased sugar levels. Their aim to "dissect out a complete neural pathway that directly senses internal energy state and modulates food-related behavioral output in the fly brain" is likely only partially achieved. While this outcome is not a shortcoming of a study per se, the depth of discussion on the mechanism of interactions between the Hugin/AstA system and the other previously characterized molecular circuit mechanisms mediating hunger-induced behavioral modulation is insufficient for readers to appreciate the novelty of this study and future challenges in the field. In this context, authors are encouraged to confront a limitation of the study due to the lack of subtype-level circuit characterization, despite their intriguing finding that only a subtype of Hugin- and AstA-releasing neurons are responsive to the elevated level of bath-applied glucose.

Reviewer #2 (Public review):

Summary:

The question of how caloric and taste information interact and consolidate remains both active and highly relevant to human health and cognition. The authors of this work sought to understand how nutrient sensing of glucose modulates sweet sensation. They found that glucose intake activates hugin signaling to AstA neurons to suppress feeding, which contributes to our mechanistic understanding of nutrient sensation. They did this by leveraging the genetic tools of Drosophila to carry out nuanced experimental manipulations and confirmed the conservation of their main mechanism in a mammalian model. This work builds on previous studies examining sugar taste and caloric sensing, enhancing the resolution of our understanding.

Strengths:

Fully discovering neural circuits that connect body state with perception remains central to understanding homeostasis and behavior. This study expands our understanding of sugar sensing, providing mechanistic evidence for a hugin/AstA circuit that is responsive to sugar intake and suppresses feeding. In addition to effectively leveraging the genetic tools of Drosophila, this study further extends their findings into a mammalian model with the discovery that NMU neural signaling is also responsive to sugar intake.

Weaknesses:

The effect of Glut1 knockdown on PER in hugin neurons is modest, and does not show a clear difference between fed and starved flies as might be expected if this mechanism acts as a sensor of internal energy state. This could suggest that glucose intake through Glut1 may only be part of the mechanism.

Reviewer #3 (Public review):

Summary:

This study identifies a novel energy-sensing circuit in Drosophila and mice that directly regulates sweet taste perception. In flies, hugin+ neurons function as a glucose sensor, activated through Glut1 transport and ATP-sensitive potassium channels. Once activated, hugin neurons release hugin peptide, which stimulates downstream Allatostatin A (AstA)+ neurons via PK2-R1 receptors. AstA+ neurons then inhibit sweet-sensing Gr5a+ gustatory neurons through AstA peptide and its receptor AstA-R1, reducing sweet sensitivity after feeding. Disrupting this pathway enhances sweet taste and increases food intake, while activating the pathway suppresses feeding.

The mammalian homolog of neuromedin U (NMU) was shown to play an analogous role in mice. NMU knockout mice displayed heightened sweet preference, while NMU administration suppressed it. In addition, VMH NMU+ neurons directly sense glucose and project to rNST Calb2+ neurons, dampening sweet taste responses. The authors suggested a conserved hugin/NMU-AstA pathway that couples energy state to taste perception.

Strengths:

Interesting findings that extend from insects to mammals. Very comprehensive.

Weaknesses:

Coupling energy status to taste sensitivity is not a new story. Many pathways appear to be involved, and therefore, it raises a question as to how this hugin-AstA pathway is unique.

Author response:

Reviewer #1 (Public review):

In this manuscript, Qin and colleagues aim to delineate a neural mechanism by which the internal satiety levels modulate the intake of sugar solution. They identified a three-step neuropeptidergic system that downregulates the sensitivity of sweet-sensing gustatory sensory neurons in sated flies. First, neurons that release a neuropeptide Hugin (which is an insect homolog of vertebrate Neuromedin U (NMU)) are in an active state when the concentration of glucose is high. This activation does not require synaptic inputs, suggesting that Hugin-releasing neurons sense hemolymph glucose levels directly. Next, the Hugin neuropeptides activate Allatostatin A (AstA)-releasing neurons via one of Hugin's receptors, PK2-R1. Finally, the released AstA neuropeptide suppresses sugar response in sugar-sensing Gr5a-expressing gustatory sensory neurons through AstA-R1 receptor. Suppression of sugar response in Gr5a-expressing neurons reduces the fly's sugar intake motivation (measured by proboscis extension reflex). They also found that NMU-expressing neurons in the ventromedial hypothalamus (VMH) of mice (which project to the rostral nucleus of the solitary tract (rNST)) are also activated by high concentrations of glucose, independent of synaptic transmission, and that injection of NMU reduces the glucose-induced activity in the downstream of NMU-expressing neurons in rNST. These data suggest that the function of Hugin neuropeptide in the fly is analogous to the function of NMU in the mouse.

Generally, their central conclusions are well-supported by multiple independent approaches. The parallel study in mice adds a unique comparative perspective that makes the paper interesting to a wide range of readers. It is easier said than done: the rigor of this study, which effectively combined pharmacological and genetic approaches to provide multiple lines of behavioral and physiological evidence, deserves recognition and praise.

A perceived weakness is that the behavioral effects of the manipulations of Hugin and AstA systems are modest compared to a dramatic shift of sugar solution-induced PER (the behavioral proxy of sugar sensitivity) induced by hunger, as presented in Figure 1B and E. It is true that the mutation of tyrosine hydroxylase (TH), which synthesizes dopamine, does not completely abolish the hunger-induced PER change, but the remaining effect is small. Moreover, the behavioral effect of the silencing of the Hugin/AstA system (Figure Supplement 13B, C) is difficult to interpret, leaving a possibility that this system may not be necessary for shifting PER in starved flies. These suggest that the Hugin-AstA system accounts for only a minor part of the behavioral adaptation induced by the decreased sugar levels. Their aim to "dissect out a complete neural pathway that directly senses internal energy state and modulates food-related behavioral output in the fly brain" is likely only partially achieved. While this outcome is not a shortcoming of a study per se, the depth of discussion on the mechanism of interactions between the Hugin/AstA system and the other previously characterized molecular circuit mechanisms mediating hunger-induced behavioral modulation is insufficient for readers to appreciate the novelty of this study and future challenges in the field.

We thank the reviewer for the thoughtful comment. We agree that the behavioral effects of manipulating the Hugin–AstA system alone were considerably weaker than the pronounced PER shifts induced by starvation. We will revise our Discussion to address it by positioning our findings within the broader context of energy regulation.

More specifically, we will discuss that feeding behavior is controlled by two distinct, yet synergistic, types of mechanisms:

(1) Hunger-driven 'accelerators': as the reviewer notes, pathways involving dopamine and NPF are powerful drivers of sweet sensitivity. These systems are strongly activated by hunger to promote food-seeking and consumption.

(2) Satiety-driven 'brakes': our study identifies the counterpart to those systems above, aka. a satiety-driven 'brake'. The Hugin–AstA pathway acts as a direct sensor of high internal energy (glucose), which is specifically engaged during satiety to actively suppress sweet sensation and prevent overconsumption.

This framework explains the seemingly discrepancy in effect size. The dramatic PER shift seen upon starvation is a combined result of engaging the 'accelerators' (hunger pathways like TH/NPF) while simultaneously releasing the 'brake' (our Hugin–AstA pathway being inactive).

Our manipulations, which specifically target only the 'brake' system, are therefore expected to have a more modest effect than this combined physiological state. Thus, rather than being a "minor part," the Hugin–AstA pathway is a mechanistically defined, satiety-specific circuit that is essential for the precise "braking" required for energy homeostasis. We will update our Discussion to emphasize how these 'accelerator' and 'brake' circuits must work in concert to ensure precise energy regulation.

In this context, authors are encouraged to confront a limitation of the study due to the lack of subtype-level circuit characterization, despite their intriguing finding that only a subtype of Hugin- and AstA-releasing neurons are responsive to the elevated level of bath-applied glucose.

We thank the reviewer for highlighting the critical issue of subtype-level specialization within the Hugin and AstA populations.

We fully agree that the Hugin system is known for its functional heterogeneity (pleiotropy), with different Hugin neuron subclusters implicated in regulating a variety of behaviors, including feeding, aversion, and locomotion (we will cite relevant literature here). Our finding that only a specific subcluster of Hugin neurons is responsive to glucose elevation provides a crucial first step in functionally dissecting this complexity. 

We will add a dedicated paragraph to elaborate on this functional partitioning. We propose that this subtype-level specialization allows the Hugin system to precisely link specific physiological states (like high circulating glucose) to appropriate behavioral outputs (like the suppression of sweet taste), demonstrating an elegant solution to coordinating multiple survival behaviors. Future work using high-resolution tools such as split-GAL4 and single-cell sequencing will be invaluable in fully mapping the specific functional roles corresponding to each Hugin and AstA subcluster.

Reviewer #2 (Public review):

Summary:

The question of how caloric and taste information interact and consolidate remains both active and highly relevant to human health and cognition. The authors of this work sought to understand how nutrient sensing of glucose modulates sweet sensation. They found that glucose intake activates hugin signaling to AstA neurons to suppress feeding, which contributes to our mechanistic understanding of nutrient sensation. They did this by leveraging the genetic tools of Drosophila to carry out nuanced experimental manipulations and confirmed the conservation of their main mechanism in a mammalian model. This work builds on previous studies examining sugar taste and caloric sensing, enhancing the resolution of our understanding.

Strengths:

Fully discovering neural circuits that connect body state with perception remains central to understanding homeostasis and behavior. This study expands our understanding of sugar sensing, providing mechanistic evidence for a hugin/AstA circuit that is responsive to sugar intake and suppresses feeding. In addition to effectively leveraging the genetic tools of Drosophila, this study further extends their findings into a mammalian model with the discovery that NMU neural signaling is also responsive to sugar intake.

Weaknesses:

The effect of Glut1 knockdown on PER in hugin neurons is modest, and does not show a clear difference between fed and starved flies as might be expected if this mechanism acts as a sensor of internal energy state. This could suggest that glucose intake through Glut1 may only be part of the mechanism.

We thank the reviewer for this insightful comment and agree that the modest behavioral effect of Glut1 knockdown is a critical finding that warrants further clarification. This observation strongly supports the idea that internal energy state is monitored by a sophisticated and robust network, not a single, fragile component. We believe the effect size is modest for two main reasons, which we will further address in revised Discussion.

Firstly, the effect size is likely attenuated by technical and molecular redundancy. Specifically, the RNAi-mediated knockdown of Glut1 may be incomplete, leaving residual transporter function. Furthermore, Glut1 is likely only one part of the Hugin neuron's intrinsic sensing mechanism; other components, such as alternative glucose transporters or downstream K_ATP channel signaling, may provide molecular redundancy, meaning that the full energy-sensing function is not easily abolished by a single manipulation.

Secondly, and more importantly, the final feeding decision is an integrated output of competing circuits. While hunger-sensing pathways like the dopamine and NPF circuits act as powerful "accelerators" to drive sweet consumption, the Hugin–AstA pathway serves as a satiety-specific "brake". The modest effect of partially inhibiting just one component of this 'brake' system is the hallmark of a precisely regulated, multi-layered homeostatic system. We will further clarify in the Discussion that the Hugin pathway represents one essential inhibitory circuit within this cooperative network that works together with the hunger-promoting systems to ensure precise control over energy intake.

Reviewer #3 (Public review):

Summary:

This study identifies a novel energy-sensing circuit in Drosophila and mice that directly regulates sweet taste perception. In flies, hugin+ neurons function as a glucose sensor, activated through Glut1 transport and ATP-sensitive potassium channels. Once activated, hugin neurons release hugin peptide, which stimulates downstream Allatostatin A (AstA)+ neurons via PK2-R1 receptors. AstA+ neurons then inhibit sweet-sensing Gr5a+ gustatory neurons through AstA peptide and its receptor AstA-R1, reducing sweet sensitivity after feeding. Disrupting this pathway enhances sweet taste and increases food intake, while activating the pathway suppresses feeding.

The mammalian homolog of neuromedin U (NMU) was shown to play an analogous role in mice. NMU knockout mice displayed heightened sweet preference, while NMU administration suppressed it. In addition, VMH NMU+ neurons directly sense glucose and project to rNST Calb2+ neurons, dampening sweet taste responses. The authors suggested a conserved hugin/NMU-AstA pathway that couples energy state to taste perception.

Strengths

Interesting findings that extend from insects to mammals. Very comprehensive.

Weaknesses:

Coupling energy status to taste sensitivity is not a new story. Many pathways appear to be involved, and therefore, it raises a question as to how this hugin-AstA pathway is unique.

The reviewer is correct that several energy-sensing pathways are known. However, we now clarify that these previously established mechanisms, such as the dopaminergic and NPF pathways, primarily function as hunger-driven "accelerators." They are activated by low energy states to promote sweet sensitivity and drive consumption.

The crucial, missing piece of the puzzle—which our study provides—is the satiety-specific "brake" mechanism. We identify the Hugin–AstA circuit as one of the “brakes”: a dedicated, central sensor that responds directly to high circulating glucose (satiety) to suppress sweet sensation and prevent overconsumption.

Thus, our work is unique because it defines the essential counterpart to the hunger pathways. In the revised Discussion, we will further explain how these 'accelerator' (hunger) and 'brake' (satiety) systems work in concert to allow for the precise, bidirectional regulation of energy intake. Furthermore, by demonstrating that this Hugin/NMU 'brake' circuit is evolutionarily conserved in mice, our findings reveal a fundamental energy-sensing strategy and suggest that this pathway could represent a promising new therapeutic target for managing conditions of excessive food intake.

eLife Assessment

This important study extends the previous interesting work of this group to address the potentially different control of movement and posture. Through experiments in which stroke participants used a robotic manipulandum, the authors provide solid evidence supporting a lack of a relation between the resting force postural bias they measure (closely related to the flexor synergy in stroke) and kinematic deficits during movement. Based on these results, the authors propose a conceptual framework that differentially weights the two main descending pathways (corticospinal tract and reticulospinal tract) for neurologically intact and stroke patients.

Reviewer #1 (Public review):

This study extends the previous interesting work of this group to address the potentially differential control of movement and posture. Their earlier work explored a broad range of data to make the case for a downstream neural integrator hypothesized to convert descending velocity movement commands into postural holding commands. Included in that data were observations from people with hemiparesis due to stroke. The current study uses similar data, but pushes into a different, but closely related direction, suggesting that these data may address the independence of these two fundamental components of motor control. The study makes observations about the different expression movement deficits during postural fixation and movement, and the different effect of force perturbations during these periods, consistent with their hypothesis that movement and postural control are separate motor functions. They speculate that the appearance of the stereotypic flexor synergies characteristic of stroke, are the result of a breakdown of this normal separation between the two control modes.

Comments on revisions:

I had only two very trivial comments in the previous version. One was simply a figure that was mistakenly not updated, and the other was the use of the terms "proximal" and "distal" to describe the location of a target. Both have been corrected.

Reviewer #2 (Public review):

The reported findings by Hadjiosif and colleagues address an important question in sensorimotor neuroscience related to the idea that movement and postural control are regulated by unique circuits. To explain the reported compromised postural control for stroke patients, the authors propose a conceptual framework that differentially weights corticospinal tract and reticulospinal tract for neurologically intact and stroke patients. Based on the currently reported findings and experimental design, the interpretation of the authors provides support to this idea.

The authors have done well to include a limitations paragraph in their discussion. While it is difficult to truly compare across many of the experimental conditions to draw any strong conclusions, the authors have included additional analyses and a limitations paragraph highlighting some weaknesses in the paper.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

This study extends the previous interesting work of this group to address the potentially differential control of movement and posture. Their earlier work explored a broad range of data to make the case for a downstream neural integrator hypothesized to convert descending velocity movement commands into postural holding commands. Included in that data were observations from people with hemiparesis due to stroke. The current study uses similar data, but pushes into a different, but closely related direction, suggesting that these data may address the independence of these two fundamental components of motor control. I find the logic laid out in the second sentence of the abstract ("The paretic arm after stroke is notable for abnormalities both at rest and during movement, thus it provides an opportunity to address the relationships between control of reaching, stopping, and stabilizing") less then compelling, but the study does make some interesting observations. Foremost among them, is the relation between the resting force postural bias and the effect of force perturbations during the target hold periods, but not during movement. While this interesting observation is consistent with the central mechanism the authors suggest, it seems hard to me to rule out other mechanisms, including peripheral ones. These limitations should should be discussed.

Thank you for summarizing our work. Note we have improved the logic in our abstract (…”providing an opportunity to ask whether control of these behaviors is independently affected in stroke”) based on your comments as outlined in our previous revision. We now extensively discuss limitations and potential alternative mechanisms in greater detail, in a dedicated section (lines 846-895; see response to reviewer 2 for further details).

Reviewer #2 (Public review):

Summary:

Here the authors address the idea that postural and movement control are differentially impacted with stroke. Specifically, they examined whether resting postural forces influenced several metrics of sensorimotor control (e.g., initial reach angle, maximum lateral hand deviation following a perturbation, etc.) during movement or posture. The authors found that resting postural forces influenced control only following the posture perturbation for the paretic arm of stroke patients, but not during movement. They also found that resting postural forces were greater when the arm was unsupported, which correlated with abnormal synergies (as assessed by the Fugl-Meyer). The authors suggest that these findings can be explained by the idea that the neural circuitry associated with posture is relatively more impacted by stroke than the neural circuitry associated with movement. They also propose a conceptual model that differentially weights the reticulospinal tract (RST) and corticospinal tract (CST) to explain greater relative impairments with posture control relative to movement control, due to abnormal synergies, in those with stroke.

Thank you for the brief but comprehensive summary. We would like to clarify one point: we do not suggest that our findings are necessarily due to the neural circuitry associated with posture being more impacted than the neural circuitry associated with movement. (rather, our conceptual model suggests that increased outflow through the (ipsilateral) RST, involved in posture, compensates for CST damage, at the expense of posture abnormalities spilling over into movement). Instead, we suggest that the neural circuitry for posture vs. movement control remains relatively separate in stroke, with impairments in posture control not substantially explaining impairments in movement control.

Comments on revisions:

The authors should be commended for being very responsive to comments and providing several further requested analyses, which have improved the paper. However, there is still some outstanding issues that make it difficult to fully support the provided interpretation.

Thank you for appreciating our response to your earlier comments. We address the outstanding issues below.

The authors say within the response, "We would also like to stress that these perturbations were not designed so that responses are directly compared to each other ***(though of course there is an *indirect* comparison in the sense that we show influence of biases in one type of perturbation but not the other)***." They then state in the first paragraph of the discussion that "Remarkably, these resting postural force biases did not seem to have a detectable effect upon any component of active reaching but only emerged during the control of holding still after the movement ended. The results suggest a dissociation between the control of movement and posture." The main issue here is relying on indirect comparisons (i.e., significant in one situation but not the other), instead of relying on direct comparisons. Using well-known example, just because one group / condition might display a significant linear relationship (i.e., slope_1 > 0) and another group / condition does not (slope_2 = 0), does not necessarily mean that the two groups / conditions are statistically different from one another [see Figure 1 in Makin, T. R., & Orban de Xivry, J. J. (2019). Ten common statistical mistakes to watch out for when writing or reviewing a manuscript. eLife, 8, e48175.].

We agree and are well aware of the limitation posed by an indirect comparison – hence the language we used to comment on the data (“did not seem”, “suggest”, etc.). To address this limitation, we performed a more direct comparison of how the two types of perturbations (moving vs. holding) interact with resting biases. For this comparison, we calculated a Response Asymmetry Index (RAI):

Above, 𝑟_𝐴 is the response on direction where resting bias is most-aligned with the perturbation, and 𝑟_𝑂 is the response on direction where resting bias is most-opposed to the perturbation.

We calculated RAIs for two response metrics used for both moving and holding perturbations: maximum deviation and time to stabilization/settling time. For these two response metrics, positive RAIs indicate an asymmetry in line with an effect of resting bias.

The idea behind the RAI is that, while the magnitude of responses may well differ between the two types of perturbations, this will be accounted for by the ratio used to calculate the asymmetry. The same approach has been used to assess symmetry/laterality across a variety of different modalities, such as gait asymmetry (Robinson et al., 1987), the relative fMRI activity in the contralateral vs. ipsilateral sensorimotor cortex while performing a motor task (Cramer et al., 1997), or the relative strength of ipsilateral vs. contralateral responses to transcranial magnetic stimulation (McPherson et al., 2018). Notably, the normalization also addresses potential differences in overall stiffness between holding vs. moving perturbations, which would similarly affect aligned and opposing cases (see our response to your following point).

Figure 8 shows RAIs we obtained for holding (red) vs. moving/pulse (blue) perturbations. For the maximum deviation (left), there is more asymmetry for the holding case though the pvalue is marginal (p=0.088) likely due to the large variability in the pulse case (individual values shown in black dots). For time to stabilization/settling time (right) the difference is significant (p=0.0048). Together, these analyses indicate that resting biases interact substantially more with holding compared to movement control, in line with a relative independence between these two control modalities. We now include this panel as Figure 8, and describe it in Results (lines 587-611).

Note that even a direct comparison does not prove that resting biases and active movement control are perfectly independent. We now discuss these issues in more depth, in the new Limitations section suggested by the Reviewer (lines 836-849).

The authors have provided reasonable rationale of why they chose certain perturbation waveforms for different. Yet it still holds that these different waveforms would likely yield very different muscular responses making it difficult to interpret the results and this remains a limitation. From the paper it is unknown how these different perturbations would differentially influence a variety of classic neuromuscular responses, including short-range stiffness and stretch reflexes, which would be at play here.

Much of the results can be interpreted when one considers classic neuromuscular physiology. In Experiment 1, differences in resting postural bias in supported versus unsupported conditions can readily be explained since there is greater muscle activity in the unsupported condition that leads to greater muscle stiffness to resist mechanical perturbations (Rack, P. M., & Westbury, D. R. (1974). The short-range stiffness of active mammalian muscle and its effect on mechanical properties. The Journal of physiology, 240(2), 331-350.). Likewise muscle stiffness would scale with changes in muscle contraction with synergies. Importantly for experiment 2, muscle stiffness is reduced during movement (Rack and Westbury, 1974) which may explain why resting postural biases do not seem to be impacting movement. Likewise, muscle spindle activity is shown to scale with extrafusal muscle fiber activity and forces acting through the tendon (Blum, K. P., Campbell, K. S., Horslen, B. C., Nardelli, P., Housley, S. N., Cope, T. C., & Ting, L. H. (2020). Diverse and complex muscle spindle afferent firing properties emerge from multiscale muscle mechanics. eLife, 9, e55177.). The concern here is that the authors have not sufficiently considered muscle neurophysiology, how that might relate to their findings, and how that might impact their interpretation. Given the differences in perturbations and muscle states at different phases, the concern is that it is not possible to disentangle whether the results are due to classic neurophysiology, the hypothesis they propose, or both. Can the authors please comment.

It is possible that neuromuscular physiology may explain part of our results. However, this would not contradict our conceptual model.

Regarding Experiment 1, it is possible that stiffness would scale with changes in background muscle contraction as the reviewer suggests. Indeed, Bennett and al.(Bennett et al., 1992) used brief perturbations on the wrist to assess elbow stiffness, finding that, during movement, stiffness was increased in positions with a higher gravity load (and, in general, in positions where the net muscle torque was higher). However, during posture maintenance (like in our Experiment 1), they found that stiffness did not vary with (elbow) position or gravity load (two characteristics of our findings in Experiment 1):

“The observed stiffness variation was not simply due to passive tissue or other joint angle dependent properties, as stiffnesses measured during posture were position invariant. Note that the minimum stiffness found in posture was higher than the peak stiffness measured during movement, and did not change much with the gravity load.” (illustrated in Fig. 5 of that paper)

We thus find it very unlikely that stiffness explains the difference between the supported vs. unsupported conditions in Experiment 1.

Even if stiffness modulation between the supported vs. unsupported conditions could explain our finding of stronger posture biases in the latter case, it would not be incompatible with our interpretation of increased RST drive: increased stiffness would potentially magnify the effects of the RST drive we propose to drive these resting biases. It is possible that the increase in resting biases under conditions of increased muscle contraction (lack of arm support) is mediated through an increase in muscle stiffness. In other words, the increase in resting biases may not directly reflect additional RST outflow per se, but the scaling, through stiffness, of the same magnitude of RST outflow. Understanding this interaction was beyond the scope of our experiment design; in line with this, we briefly comment about it in our Limitations section.

Regarding Experiment 2, stiffness has indeed been shown to be lower during movement, and we now comment the potential effect of this on our results in the “Limitations” section (lines 815-830, replicated below). Importantly, for the case of holding perturbations, the increased stiffness associated with holding would increase resistance to both extension and flexion-inducing perturbations. Thus, higher stiffness would be unlikely to explain our finding whereby resting biases resist or aggravate the effects of holding perturbations depending on perturbation direction. In addition, the framework in Blum et al., that describes how interactions between alpha and gramma drive can explain muscle activity patterns, does not rule out central neural control of stiffness: “muscle spindles have a unique muscle-within-muscle design such that their firing depends critically on both peripheral and central factors” (emphasis ours). It may be, for example, that gamma motoneurons controlling muscle spindles and stiffness are modulated from input from the reticular formation, making this a mechanism in line with our conceptual model.

“Moreover, it has been shown that joint stiffness is reduced during movement compared to holding control (Rack and Westbury, 1974; Bennett et al., 1992). Along similar lines, muscle spindle activity – which may modulate stiffness – scales with extrafusal muscle fiber activity (such as muscle exertion involved in holding) and forces acting through the tendon (Blum et al., 2020). Such observations could, in principle, explain why we were unable to detect a relationship between resting biases and active movement control but we readily found a relationship between resting biases and active holding control: reduced joint stiffness during movement could scale down the influence of resting abnormalities. There are two issues with this explanation, however. First, it is debatable whether this should be considered an alternative explanation per se: stiffness modulation could be, in total or in part, the manifestation of a central movement/posture CST/RST mechanism similar to the one we propose in our conceptual model. For example, (Blum et al., 2020) argue that muscle spindle firing depends on both peripheral and central factors. Second, increased stiffness would not necessarily help detect differences in how active postural control responds to within-resting-posture vs. out-of-resting-posture perturbations. This is because an overall increase in stiffness would likely increase resistance to perturbations in any direction.”

The authors should provide a limitations paragraph. They should address 1) how they used different perturbation force profiles, 2) the muscles were in different states which would change neuromuscular responses between trial phase / condition, 3) discuss a lack of direct statistical comparisons that support their hypothesis, and 4) provide a couple of paragraphs on classic neurophysiology, such as muscle stiffness and stretch reflexes, and how these various factors could influence the findings (i.e., whether they can disentangle whether the reported results are due to classic neurophysiology, the hypothesis they propose, or both).

Thank you for your suggestion. We now discuss these points in a separate paragraph (lines 846895), bringing together our previous discussion on stretch reflexes, our description of different perturbation types, and the additional issues raised by the reviewer above.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have responded well to all my concerns, save two minor points.

Figure 2 appears to be unchanged, although they describe appropriate changes in the response letter.

Thank you for catching this error – we now include the updated figure (further updated to use the terms near/distant in place of proximal/distal).

I still take issue with the use of proximal and distal to describe the locations of targets. Taking definitions somewhat randomly from the internet, "The terms proximal and distal are used in structures that are considered to have a beginning and an end," and "Proximal and distal are anatomical terms used to describe the position of a body part in relation to another part or its origin." In any case, the hand does not become proximal just because you bring it to your chest. Why not simply stick to the common and clearly defined terms "near" and "distant"?

Point taken. We have updated the paper to use the terms near/distant.

Additional changes/corrections not outlined above

We now include a link to the data and code supporting our findings (https://osf.io/hufy8/). In addition, we made several minor edits throughout the text to improve readability, and corrected occasional mislabeling of CCW and CW pulse data. Note that this correction did not alter the (lack of) relationship between resting biases and responses to perturbations during active movement.

Response letter references

Bennett D, Hollerbach J, Xu Y, Hunter I (1992) Time-varying stiffness of human elbow joint during cyclic voluntary movement. Exp Brain Res 88:433–442.

Blum KP, Campbell KS, Horslen BC, Nardelli P, Housley SN, Cope TC, Ting LH (2020) Diverse and complex muscle spindle afferent firing properties emerge from multiscale muscle mechanics. Elife 9:e55177.

Cramer SC, Nelles G, Benson RR, Kaplan JD, Parker RA, Kwong KK, Kennedy DN, Finklestein SP, Rosen BR (1997) A functional MRI study of subjects recovered from hemiparetic stroke. Stroke 28:2518–2527.

McPherson JG, Chen A, Ellis MD, Yao J, Heckman C, Dewald JP (2018) Progressive recruitment of contralesional cortico-reticulospinal pathways drives motor impairment post stroke. J Physiol 596:1211–1225 Available at: https://doi.org/10.1113/JP274968.

Rack PM, Westbury D (1974) The short range stiffness of active mammalian muscle and its effect on mechanical properties. J Physiol 240:331–350.

Robinson R, Herzog W, Nigg BM (1987) Use of force platform variables to quantify the effects of chiropractic manipulation on gait symmetry. J Manipulative Physiol Ther 10:172–176.

Williams PE, Goldspink G (1973) The effect of immobilization on the longitudinal growth of striated muscle fibres. J Anat 116:45.

eLife Assessment

This study investigates how people adapt their speech when auditory feedback is altered. The analyses are rigorous and the work makes a valuable contribution by extending methods from limb motor control to speech. However, because the paradigm does not directly measure sensory error, the evidence for the proposed mechanism of sensorimotor learning is incomplete. The findings are best viewed as evidence for how prior motor adjustments influence subsequent behaviour, highlighting the need for future studies to more precisely separate sensory and motor contributions to adaptation.

Reviewer #1 (Public review):

Summary:

In this submitted manuscript, Lu, Tang, and colleagues implement a novel serial perturbation paradigm during speech to isolate the effects of sensory and motor processes on compensation. They perform three main studies: in the first study, they validate their method by randomly perturbing pitch in a series of produced vowels. They demonstrate that the amount of perturbation is driven (in part) by the previous trial's amount of motor compensation applied as opposed to the sensory perturbation. In the second experiment, they found that this effect carries over to single vowel words, but the effect was much weaker when different words were produced. Thirdly, the authors reproduce these findings in a more linguistically relevant way (during sentences) and show that the previously shown compensation effect only occurs within syntactic structures and not across them, suggesting an interplay between sensorimotor systems and linguistic structure processing.

Strengths:

Overall, this is a very unique study and strikes me as being potentially quite impactful. The authors have performed a large number of experiments to validate their findings that provide novel insights into the processes underlying compensation during speech production. These findings are also likely to produce new avenues for studying the neural mechanisms that support these processes.

Weaknesses:

While the authors go to great lengths to disassociate the serial effects of sensory and motor compensation, which is commendable, one weakness is that they are intrinsically linked (motor actions produce sensory consequences). Therefore, there is no obvious way to decouple them for the purposes of investigation. It would be beneficial to discuss future research that could further disentangle these factors.

Reviewer #2 (Public review):

This study aims to disentangle the contribution of sensory and motor processes (mapped onto the inverse and forward components of speech motor control models like DIVA) to production changes as a result of altered auditory feedback. After five experiments, the authors conclude that it is the motor compensation on the previous trial, and not the sensory error, that drives compensatory responses in subsequent trials.

Assessment:

The goal of this paper is great, and the question is timely. Quite a bit of work has gone into the study, and the technical aspects are sound. That said, I just don't understand how the current design can accomplish what the authors have set as their goal. This may, of course, be a misunderstanding on my part, so I'll try to explain my confusion below. If it is indeed my mistake, then I encourage the authors to dedicate some space to unpacking the logic in the Introduction, which is currently barely over a page long. They should take some time to lay out the logic of the experimental design and the dependent and independent variables, and how this design disentangles sensory and motor influences. Then clearly discuss the opposing predictions supporting sensory-driven vs. motor-driven changes. Given that I currently don't understand the logic and, consequently, the claims, I will focus my review on major points for now.

Main issues

(1) Measuring sensory change. As acknowledged by the authors, making a motor correction as a function of altered auditory feedback is an interactive process between sensory and motor systems. However, one could still ask whether it is primarily a change to perception vs. a change to production that is driving the motor correction. But to do this, one has to have two sets of measurements: (a) perceptual change, and (b) motor change. As far as I understand, the study has the latter (i.e., C), but not the former. Instead, the magnitude of perceptual change is estimated through the proxy of the magnitude of perturbation (P), but the two are not the same; P is a physical manipulation; perceptual change is a psychological response to that physical manipulation. It is theoretically possible that a physical change does not cause a psychological change, or that the magnitude of the two does not match. So my first confusion centers on the absence of any measure of sensory change in this study.

To give an explicit example of what I mean, consider a study like Murphy, Nozari, and Holt (2024; Psychonomic Bulletin & Review). This work is about changes to production as a function of exposure to other talkers' acoustic properties - rather than your own altered feedback - but the idea is that the same sensory-motor loop is involved in both. When changing the acoustic properties of the input, the authors obtain two separate measures: (a) how listeners' perception changes as a function of this physical change in the acoustics of the auditory signal, and (b) how their production changes. This allows the authors to identify motor changes above and beyond perceptual changes. Perhaps making a direct comparison with this study would help the reader understand the parallels better.

(2) A more fundamental issue for me is a theoretical one: Isn't a compensatory motor change ALWAYS a consequence of a perceptual change? I think it makes sense to ask, "Does a motor compensation hinge on a previous motor action or is sensory change enough to drive motor compensation?" This question has been asked for changed acoustics for self-produced speech (e.g., Hantzsch, Parrell, & Niziolek, 2022) and other-produced speech (Murphy, Holt, & Nozari, 2025), and in both cases, the answer has been that sensory changes alone are, in fact, sufficient to drive motor changes. A similar finding has been reported for the role of cerebellum in limb movements (Tseng et al., 2007), with a similar answer (note that in that study, the authors explicitly talk about "the addition" of motor corrections to sensory error, not one vs. the other as two independent factors. So I don't understand a sentence like "We found that motor compensation, rather than sensory errors, predicted the compensatory responses in the subsequent trials", which views motor compensations and sensory errors as orthogonal variables affecting future motor adjustments.

In other words, there is a certain degree of seriality to the compensation process, with sensory changes preceding motor corrections. If the authors disagree with this, they should explain how an alternative is possible. If they mean something else, a comparison with the above studies and explaining the differences in positions would greatly help.

(3) Clash with previous findings. I used the examples in point 2 to bring up a theoretical issue, but those examples are also important in that all three of them reach a conclusion compatible with one another and different from the current study. The authors do discuss Tseng et al.'s findings, which oppose their own, but dismiss the opposition based on limb vs. articulator differences. I don't find the authors reasoning theoretically convincing here, but more importantly, the current claims also oppose findings from speech motor studies (see citations in point 2), to which the authors' arguments simply don't apply. Strangely, Hantzsch et al.'s study has been cited a few times, but never in its most important capacity, which is to show that speech motor adaptation can take place after a single exposure to auditory error. Murphy et al. report a similar finding in the context of exposure to other talkers' speech.

If the authors can convincingly justify their theoretical position in 2, the next step would be to present a thorough comparison with the results of the three studies above. If indeed there is no discrepancy, this comparison would help clarify it.

References

Hantzsch, L., Parrell, B., & Niziolek, C. A. (2022). A single exposure to altered auditory feedback causes observable sensorimotor adaptation in speech. eLife, 11, e73694.

Murphy, T. K., Nozari, N., & Holt, L. L. (2024). Transfer of statistical learning from passive speech perception to speech production. Psychonomic Bulletin & Review, 31(3), 1193-1205.

Murphy, T. K., Holt, L. L. & Nozari, N. (2025). Exposure to an Accent Transfers to Speech Production in a Single Shot. Preprint available at: https://papers.ssrn.com/sol3/papers.cfm?abstract_id=5196109.

Tseng, Y. W., Diedrichsen, J., Krakauer, J. W., Shadmehr, R., & Bastian, A. J. (2007). Sensory prediction errors drive cerebellum-dependent adaptation of reaching. Journal of neurophysiology, 98(1), 54-62.

eLife Assessment

This study extends prior work on head bristle mechanosensation by delivering a synaptic-resolution map of second-order partners that preserves somatotopy and highlights a cholinergic pathway linking sensory input to grooming circuits, providing a valuable resource for the field. The reconstructions and quantitative connectivity analyses provide solid support the main anatomical claims, while causal sufficiency for the behavioral sequence remains inferential and could be strengthened by a simple rank-order test relating wiring to the known grooming hierarchy.

Reviewer #1 (Public review):

Summary:

Calle-Schuler et. al. reconstruct all the pre- and post-synaptic neurons to the bristle mechanosensory neurons on the adult fly head to understand how neural circuits determine the sequential motor patterns during fly grooming. They find that most presynaptic neurons, interneurons, and excitatory postsynaptic neurons are also somatotopically organized, such that each neuron is more connected to bristles mechanosensory neurons that are closer on the head and less connected to bristles mechanosensory neurons that are further away. These include the direct BMN-BMN circuits, excitatory interneurons, as well as the inhibitory networks. They also identify that the entire hemi-lineage 23b forms excitatory postsynaptic circuits with BMNs, highlighting how these circuits and hence their function could be developmentally determined.

Strengths:

This is a complete map of all the neurons that make 5 or more pre- and post-synaptic connections of the fly head BMNs. Using this, the authors have identified various trends, such as ascending neurons providing most of the GABAergic inhibitory input, which could provide the presynaptic inhibition essential for the parallel model for sequential grooming generation. Moreover, they identified that the entire cholinergic hemilineage 23b is postsynaptic to BMNs.

Weaknesses:

Although the somatotropic organization is an elegant mechanism to generate sequential motor sequences during grooming, none of the analyses in the paper directly demonstrate that this somatotropic connectivity is sufficient to generate hierarchical suppression and reconstruct the grooming sequence. If somatotropic organization is sufficient, then hierarchical clustering should recover the grooming sequence. Their detailed connectome enables the authors to test if some networks are more crucial for grooming sequence than others: to what extent can each network individually (ascending neurons-BMN alone) or a combination (BMN-BMN, ascending-BMN, BMN-descending, etc.) recover the sequence observed during grooming. If all the pre- and post-synaptic neurons put together cannot explain the sequence, then the sequence is probably determined by individual synaptic strengths or other key downstream neurons.

Reviewer #2 (Public review):

Summary:

Schuler et al. present an extensive analysis of the synaptic connectivity of mechanosensory head bristles in the brain of Drosophila melanogaster. Based on the previously described set of bristle afferent neurons, (BMNs), located on the head, the study aims to provide a complete, quantitative assessment of all synaptic partners in the ventral brain. Activation of head bristles induces grooming behavior, which is hierarchically organized, and hypothesized to be grounded in a parallel cellular architecture in the central brain. The authors found evidence that, at the synaptic level, neurons downstream of the BMN afferents, namely the postsynaptic LB23 interneurons and recurrent GABAergic neurons (involved in sensory gain control), are organized in parallel, following the somatotopic organization described for the BMN afferents. This study, therefore, represents an important step towards a better understanding of the cellular circuits that govern the hierarchical order of sequentially organized grooming behavior in Drosophila melanogaster.

The study is well done, the images are well designed and extensive in number, but the account is challenging to read and digest for the reader outside the Drosophila /connectome community. It is amazing what can be done with the connectome nowadays using the up-to-date FAFB dataset, the analytical and visual tools (as in FlyWire), in combination with known anatomy/physiology/behavior in DM. I suggest that the authors provide more detail on hemilineages, their relationship to the FAB connectome, the predicted neurotransmitter identity, and the use of statistical CatMAID tools used in some of the Figures.

A graphical summary at the end of the study would be very useful to highlight the important findings focusing on neuron populations identified in this study and their position in the hypothesized parallel central circuitry of BMNs.

Reviewer #3 (Public review):

Summary:

The authors set out to extend their previous mapping of Drosophila head mechanosensory neurons (Eichler et al., 2024) by reconstructing their full second-order connectome. Their aim is to reveal how bristle mechanosensory neurons (BMNs) interface with excitatory and inhibitory partners to generate location-specific grooming movements, and to identify the circuit motifs and developmental lineages that support this transformation.

Strengths:

The strengths of this work are clear. The authors present a comprehensive synaptic-resolution connectome for BMNs, identifying nearly all of their pre- and postsynaptic partners. This dataset reveals important circuit motifs:

(1) BMNs provide feedforward excitation to descending neurons, feedforward inhibition to interneurons, and are themselves strongly regulated by GABAergic presynaptic inhibition.

(2) These motifs together support the idea that BMN activity is locally gated and hierarchically suppressed, fitting well with known behavioural sequences of grooming.

(3) The study also shows that connectivity preserves somatotopy, such that BMNs from neighbouring bristle populations converge onto shared partners, while distant BMNs remain segregated.

(4) A developmental analysis reveals both primary and secondary partners, suggesting a layered scaffold plus adult-specific elaborations.

(5) Finally, the identification of hemilineage 23b (LB23) as a core postsynaptic pathway - incorporating previously described antennal grooming neurons (aBN2) - provides a striking link between developmental lineage, anatomical connectivity, and behavioral output.

(6) Together, the dataset represents a valuable resource for the neuroscience community and a foundation for future functional studies.

Weaknesses:

There are also some weaknesses that mostly only limit clarity.

(1) The writing is dense, with results often presented in a cryptic fashion and the functional implications deferred to the discussion. As a result, the significance of circuit motifs such as BMN→motor or reciprocal inhibitory loops is sometimes buried, rather than highlighted when first described.

(2) Some assumptions require more explanation for non-specialist readers - for example, how bristle identity is inferred in EM in the absence of cuticular structures, or what is meant by "ascending" and "descending" in a dataset that does not include the ventral nerve cord. While some of this comes from the earlier paper, it would help readers of this one to explain this.

(3) Visualization choices also sometimes obscure key conclusions: network graphs can be visually appealing but do not clearly convey somatotopy or BMN-type differences; heatmaps or region-level matrices would make the parallel, block-like organization of the circuit more evident.

(4) The data might also speak to roles beyond grooming (e.g., mechanosensory modulation of posture or feeding), and a brief acknowledgement of this would broaden the impact.

(5) The restriction to one hemisphere should be explicitly acknowledged as a limitation when framing this as a 'comprehensive' connectome.

Overall, the authors achieve their main goal: they convincingly show that BMNs connect into parallel, somatotopically organized pathways, with LB23 providing a key lineage-based link from sensory input to grooming output. The dataset is carefully analyzed, and while the presentation could be streamlined, the connectome will be a valuable resource for researchers studying sensory processing, motor control, and the logic of circuit organization.

eLife Assessment

This timely and fundamental study introduces a human iPSC-based co-culture system that models Kupffer cell-hepatocyte interactions and aims to recapitulate liver-specific immune-parenchymal dynamics. Direct contact between iMacs and iHeps promotes mutual tissue-specific maturation, with iHeps downregulating fetal genes while iMacs acquire a Kupffer cell-like profile. This convincing in vitro model holds significant promise and is a leap forward; future experimental understanding will enhance its translational impact.

Reviewer #1 (Public review):

The manuscript presents a compelling new in vitro system based on isogenic co-cultures of human iPSC-derived hepatocytes and macrophages, enabling the modelling of hepatic immune responses with unprecedented physiological relevance. The authors show that co-culture leads to enhanced maturation of hepatocytes and tissue-resident macrophage identity, which cannot be achieved through conditioned media alone. Using this system, they functionally validate immune-driven hepatotoxic responses to a panel of drugs and compare the system's predictive power to that of monocyte-derived macrophages. The results underscore the necessity of macrophage-hepatocyte crosstalk for accurate modelling of liver inflammation and drug toxicity in vitro.

The manuscript is clearly written and addresses a key limitation in liver organoid systems: the lack of immune complexity and tissue-specific macrophage imprinting. Nevertheless, several conclusions would benefit from a more careful interpretation of the data, and some important controls or explanations are missing, particularly in the flow cytometry gating strategies, stress marker validation, and cluster interpretations.

Strengths:

(1) Novelty and Relevance: The study presents a highly innovative co-culture system based on isogenic human iPSCs, addressing an unmet need in modelling immune-mediated hepatotoxicity.

(2) Mechanistic Insight: The reciprocal reprogramming between iHeps and iMacs, including induction of KC-specific pathways and hepatocyte maturation markers, is convincingly demonstrated.

(3) Functional Readouts: The application of the model to detect IL-6 responses to hepatotoxic compounds enhances its translational relevance.

Weaknesses:

(1) Several key claims, particularly those derived from PCA plots and DEG analyses, are overinterpreted and require more conservative language or further validation.

(2) The purity of sorted hepatocytes and macrophages is not convincingly demonstrated; contamination across gates may confound transcriptomic readouts.

(3) Stress response genes and ER stress/apoptosis signatures are not properly assessed, despite being potentially activated in the system.

(4) Some figure panels and legends lack statistical annotations, and microscopy validation of morphological changes is missing.

(5) The co-culture model with monocyte-derived macrophages is not fully characterised, making comparisons less informative.

Reviewer #2 (Public review):

Summary:

This study builds on work by Glass and Guilliams showing that mouse Kupffer cells depend on the surrounding cells, including endothelium, hepatocytes, and stellate cells, for their identity. Herein, the authors extend the work to human systems. It nicely highlights why taking monocyte-derived macrophages and pretending they are Kupffer cells is simply misleading.

Strengths:

Many, including human cells, difficult culture assays, and important new data.

Weaknesses:

This reviewer identified minor queries only, rather than 'weaknesses' as such.

Reviewer #3 (Public review):

Summary:

In this study, the authors establish a human in vitro liver model by co-culturing induced hepatocyte-like cells (iHEPs) with induced macrophages (iMACs). Through flow cytometry-based sorting of cell populations at days 3 and 7 of co-culture, followed by bulk RNA sequencing, they demonstrate that bidirectional interactions between these two cell types drive functional maturation. Specifically, the presence of iMACs accelerates the hepatic maturation program of iHEPs, while contact-dependent cues from iHEPs enhance the acquisition of Kupffer cell identity in iMACs, indicating that direct cell-cell interactions are critical for establishing tissue-resident macrophage characteristics.

Functionally, the authors show that iMAC-derived Kupffer-like cells respond to pathological stimuli by producing interleukin-6 (IL-6), a hallmark cytokine of hepatic immune activation. When exposed to a panel of clinically relevant hepatotoxic drugs, the co-culture system exhibited concentration-dependent modulation of IL-6 secretion consistent with reported drug-induced liver injury (DILI) phenotypes. Notably, this response was absent when hepatocytes were co-cultured with monocyte-derived macrophages from peripheral blood, underscoring the liver-specific phenotype and functional relevance of the iMAC-derived Kupffer-like cells. Collectively, the study proposes this co-culture platform as a more physiologically relevant model for interrogating macrophage-hepatocyte crosstalk and assessing immune-mediated hepatotoxicity in vitro.

Strengths:

A major strength of this study lies in its systematic dissection of cell-cell interactions within the co-culture system. By isolating each cell type following co-culture and performing comprehensive transcriptomic analyses, the authors provide direct evidence of bidirectional crosstalk between iMACs and iHEPs. The comparison with single-culture controls is particularly valuable, as it clearly demonstrates how co-culture enhances functional maturation and lineage-specific gene expression in both cell types. This approach allows for a more mechanistic understanding of how hepatocyte-macrophage interactions contribute to the acquisition of tissue-specific phenotypes.

Weaknesses:

(1) Overreliance on bulk RNA-seq data:

The primary evidence supporting cell maturation is derived from bulk RNA sequencing, which has inherent limitations in resolving heterogeneous cellular states and functional maturation. The conclusions regarding hepatocyte maturation are based largely on increased expression of a subset of CYP genes and decreased AFP levels - markers that, while suggestive, are insufficient on their own to substantiate functional maturation. Additional phenotypic or functional assays (e.g., metabolic activity, protein-level validation) would significantly strengthen these claims.

(2) Insufficient characterization of input cell populations:

The manuscript lacks adequate validation of the cellular identities prior to co-culture. Although the authors reference previously published protocols for generating iHEPs and iMACs, it remains unclear whether the cells used in this study faithfully retain expected lineage characteristics. For example, hepatocyte preparations should be characterized by flow cytometry for ALB and AFP expression, while iMACs should be assessed for canonical macrophage markers such as CD45, CD11b, and CD14 before co-culture. Without these baseline data, it is difficult to interpret the magnitude or significance of any co-culture-induced changes.

(3) Quantitative assessment of IL-6 production is insufficient:

The analysis of drug-induced IL-6 responses is based primarily on relative changes compared to control conditions. However, percentage changes alone are inadequate to capture the biological relevance of these responses. Absolute cytokine production levels - particularly in response to LPS stimulation - should be reported and directly compared to PBMC-derived macrophages to determine whether iMAC-derived Kupffer-like cells exhibit enhanced cytokine output. Moreover, the Methods section should clearly describe how ELISA results were normalized or corrected to account for potential differences in cell number, viability, or culture conditions.

(4) Unclear mechanistic interpretation of IL-6 modulation:

The observed changes in IL-6 production upon drug treatment cannot be interpreted solely as evidence of Kupffer cell-specific functionality. For instance, IL-6 suppression by NSAIDs such as diclofenac is well known to result from altered prostaglandin synthesis due to COX inhibition, while leflunomide's effects are linked to metabolite-induced modulation of immune cell proliferation and broader cytokine networks. These mechanisms are distinct from Kupffer cell identity and may not directly reflect liver-specific macrophage function. Consequently, changes in IL-6 secretion alone - particularly without additional mechanistic evidence or analysis of other cytokines - are insufficient to conclude that co-culture with hepatocytes drives the acquisition of bona fide Kupffer cell maturity.

Author response:

Reviewer #1:

In line with the reviewer’s suggestions, we will be adjusting the text with more conservative language regarding the claims of maturation within the co-culture system, and emphasize that the conclusion is based on limited transcriptomic evidence. We acknowledge that the results from bulk RNA sequencing might contain contaminants across the gates, but would like to point out that the CD45+ CD14+ population is clear, and any resulting contamination would likely be small. We will be addressing this caveat clearly in a new limitations section, as suggested by reviewer 3 as well. We will also be taking the reviewer’s suggestion to look further into the stress response genes to further characterize the system. We apologise if we might have missed out any statistical annotations and will take care to include them in the updated version.

Reviewer #3:

We acknowledge the reviewer’s concerns that the study was primarily focused on bulk RNA sequencing data and might not fully represent the complex metabolic and functional shifts, especially in a cell type like the hepatocyte , and will be addressing these concerns in a new limitations section in the revised manuscript. We also apologise if it was unclear in the manuscript that the iHeps and iMacs were characterised prior to coculturing, for example the iMacs are routinely assessed for CD45, CD14 and CD163 prior to the start of any experiment, and likewise the iHeps are tested by qPCR, which also served as the baseline of the fold expression changes in Fig 3. The primary aim of the IL-6 assays is to demonstrate that the hepatocyte co-culture systems behave differently based on the source of the macrophages, and that the use of primary macrophages might not be suitable in studying drug responses in-vitro. We will clarify in the revised manuscript that the overall effect might not be directly related to specific Kupffer cell identity.

eLife Assessment

This study constitutes a fundamental advance for the uveal melanoma research field that might be exploited to target this deadly cancer and more generally for targeting transcriptional dependency in cancers. This work substantially advances our understanding of pharmacological inhibition of SWI/SNF as a therapeutic approach for cancer. The study is well written and provides compelling evidence, including comprehensive datasets, compound screens, gene expression analysis, epigenetics, as well as animal studies.

Reviewer #1 (Public review):

Summary:

The presented study by Centore and colleagues investigates the inhibition of BAF chromatin remodeling complexes. The study is well written and includes comprehensive datasets, including compound screens, gene expression analysis, epigenetics, as well as animal studies. This is an important piece of work for the uveal melanoma research field, and sheds light on a new inhibitor class, as well as a mechanism that might be exploited to target this deadly cancer for which no good treatment options exist.

Strengths:

This is a comprehensive and well-written study.

Reviewer #2 (Public review):

Summary:

The authors generate an optimized small molecule inhibitor of SMARCA2/4 and test it in a panel of cell lines. All uveal melanoma (UM) cell lines in the panel are growth inhibited by the inhibitor making the focus of the paper. This inhibition is correlated with loss of promoter occupancy of key melanocyte transcription factors e.g. SOX10. SOX10 overexpression and a point mutation in SMARCA4 can rescue growth inhibition exerted by the SMARCA2/4 inhibitor. Treatment of a UM xenograft model results in growth inhibition and regression which correlates with reduced expression of SOX10 but not discernible toxicity in the mice. Collectively, the data suggest a novel treatment of uveal melanoma.

Strengths:

There are many strengths of the study, including the strong challenge of the on-target effect, the assays used and the mechanistic data. The results are compelling as are the effects of the inhibitor. The in vivo data is dose-dependent and doses are low enough to be meaningful and associated with evidence of target engagement.

Reviewer #3 (Public review):

Summary:

This manuscript reports the discovery of new compounds that selectively inhibit SMARCA4/SMARCA2 ATPase activity and have pronounced effects on uveal melanoma cell proliferation. They induce apoptosis and suppress tumor growth, with no toxicity in vivo. The report provides biological significance by demonstrating that the drugs alter chromatin accessibility at lineage specific gene enhancer regions and decrease expression of lineage specific genes, including SOX10 and SOX10 target genes.

Strengths:

The study provides compelling evidence for the therapeutic use of these compounds and does a thorough job at elucidating the mechanisms by which the drugs work. The study will likely have a high impact on the chromatin remodeling and cancer fields. The datasets will be highly useful to these communities.

[Editors' note: The authors have addressed all of the outstanding issues.]

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review): 

Summary: 

The presented study by Centore and colleagues investigates the inhibition of BAF chromatin remodeling complexes. The study is well written and includes comprehensive datasets, including compound screens, gene expression analysis, epigenetics, as well as animal studies. This is an important piece of work for the uveal melanoma research field, and sheds light on a new inhibitor class, as well as a mechanism that might be exploited to target this deadly cancer for which no good treatment options exist. 

Strengths: 

This is a comprehensive and well-written study. 

Weaknesses: 

There are minimal weaknesses. 

Reviewer #2 (Public review): 

Summary: 

The authors generate an optimized small molecule inhibitor of SMARCA2/4 and test it in a panel of cell lines. All uveal melanoma (UM) cell lines in the panel are growth inhibited by the inhibitor making the focus of the paper. This inhibition is correlated with loss of promoter occupancy of key melanocyte transcription factors e.g. SOX10. SOX10 overexpression and a point mutation in SMARCA4 can rescue growth inhibition exerted by the SMARCA2/4 inhibitor. Treatment of a UM xenograft model results in growth inhibition and regression which correlates with reduced expression of SOX10 but not discernible toxicity in the mice. Collectively, the data suggest a novel treatment of uveal melanoma. 

Strengths: 

There are many strengths of the study, including the strong challenge of the on-target effect, the assays used and the mechanistic data. The results are compelling as are the effects of the inhibitor. The in vivo data is dose-dependent and doses are low enough to be meaningful and associated with evidence of target engagement. 

Weaknesses: 

The authors have addressed weaknesses in the revised version. 

Reviewer #3 (Public review): 

Summary: 

This manuscript reports the discovery of new compounds that selectively inhibit SMARCA4/SMARCA2 ATPase activity and have pronounced effects on uveal melanoma cell proliferation. They induce apoptosis and suppress tumor growth, with no toxicity in vivo. The report provides biological significance by demonstrating that the drugs alter chromatin accessibility at lineage specific gene enhancer regions and decrease expression of lineage specific genes, including SOX10 and SOX10 target genes. 

Strengths: 

The study provides compelling evidence for the therapeutic use of these compounds and does a thorough job at elucidating the mechanisms by which the drugs work. The study will likely have a high impact on the chromatin remodeling and cancer fields. The datasets will be highly useful to these communities. 

Weaknesses: 

The authors have addressed all my concerns. 

Recommendations for the authors: 

We would, however, like to draw the authors attention to 2 comments by the referees. 

Referee 1 comments: While BAP1 mutant UM cell lines were included for some of the experiments, it seems the in-vivo data mentioned in the response to the reviewers comment is missing? The authors stated that "MP46 (Supplementary Fig. 3a) is BAP1null uveal melanoma cell line with no detectable protein expression (AmiroucheneAngelozzi et al., Mol Oncol 2014), and we have observed strong tumor growth inhibition in this CDX model with our BAF ATPase inhibitor." But the CDX model data shown in Figure 4 is from 92.1 cells. If this data is available, then the manuscript would benefit from its addition. 

We thank the reviewer for bringing this to our attention. As the reviewer mentioned, we show 92-1 CDX model in our manuscript. Additionally, strong tumor growth inhibition was observed in MP-46  CDX model treated with our BAF ATPase inhibitor and can be found in Vaswani et al., 2025 (PMID:39801091, https://pubmed.ncbi.nlm.nih.gov/39801091/).

Referee 3 comments: 

Supplementary Figure 2C 

Is the T910M mutation in the parental MP41 cells heterozygous? If so, the authors should indicate this in the figure legend. If this is a homozygous mutation, the authors should explain how the inhibitors suppress SMARCA4 activity in cells that have a LOF mutation. 

Could the authors please comment on these issues before a final version is posted online? 

We thank the reviewer for bringing this to our attention. T910M mutation is heterozygous and the variant allele frequency for that mutation is 0.5. We updated the figure legend accordingly to reflect the genotype of the mutations highlighted in the table.

Reviewer #1 (Recommendations for the authors): 

The authors have addressed most of the questions in their review. 

While BAP1 mutant UM cell lines were included for some of the experiments, it seems the in-vivo data mentioned in the response to the reviewers comment is missing? The authors stated that "MP46 (Supplementary Fig. 3a) is BAP1-null uveal melanoma cell line with no detectable protein expression (Amirouchene-Angelozzi et al., Mol Oncol 2014), and we have observed strong tumor growth inhibition in this CDX model with our BAF ATPase inhibitor." But the CDX model data shown in Figure 4 is from 92.1 cells. If this data is available, then the manuscript would benefit from its addition. 

Reviewer #3 (Recommendations for the authors): 

Supplementary Figure 2C 

Is the T910M mutation in the parental MP41 cells heterozygous? If so, the authors should indicate this in the figure legend. If this is a homozygous mutation, the authors should explain how the inhibitors suppress SMARCA4 activity in cells that have a LOF mutation.

eLife Assessment

This manuscript provides a single-cell transcriptomic atlas for AML (222 samples comprising 748,679 cells) integrating data from multiple studies. They use this dataset to investigate t(8;21) AML, and they reconstruct the Gene Regulatory Network and enhancer Gene Regulatory Network, which allowed identification of interesting targets. This aggregation is important and can help infer differences in genetic regulatory modules based on the age of disease onset. Their compelling effort may help explain age-related variations in prognosis and disease development in subtype-specific manner.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors performed an integration of 48 scRNA-seq public datasets and created a single-cell transcriptomic atlas for AML (222 samples comprising 748,679 cells). This is important since most AML scRNA-seq studies suffer from small sample size coupled with high heterogeneity. They used this atlas to further dissect AML with t(8;21) (AML-ETO/RUNX1-RUNX1T1), which is one of the most frequent AML subtypes in young people. In particular, they were able to predict Gene Regulatory Networks in this AML subtype using pySCENIC, which identified the paediatric regulon defined by a distinct group of hematopoietic transcription factors (TFs) and the adult regulon for t(8;21). They further validated this in bulk RNA-seq with AUCell algorithm and inferred prenatal signature to 5 key TFs (KDM5A, REST, BCLAF1, YY1, and RAD21), and the postnatal signature to 9 TFs (ENO1, TFDP1, MYBL2, KLF1, TAGLN2, KLF2, IRF7, SPI1, and YXB1). They also used SCENIC+ to identify enhancer-driven regulons (eRegulons), forming an eGRN, and found that prenatal origin shows a specific HSC eRegulon profile, while a postnatal shows a GMP profile. They also did an in silico perturbation and found AP-1 complex (JUN, ATF4, FOSL2), P300 and BCLAF1 as important TFs to induce differentiation. Overall, I found this study very important in creating a comprehensive resource for AML research.

Strengths:

• The generation of an AML atlas integrating multiple datasets with almost 750K cells will further support the community working on AML

• Characterisation of t(8;21) AML proposes new interesting leads.

• The t(8;21) TFs/regulons identified from any of the single dataset are not complete and now the authors showed that the increase in the number of cells that allowed identification of novel ones.

Comments on revisions:

In the revised version of the manuscript, the authors addressed all my comments.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review): 

Summary: 

In this manuscript, the authors performed an integration of 48 scRNA-seq public datasets and created a single-cell transcriptomic atlas for AML (222 samples comprising 748,679 cells). This is important since most AML scRNA-seq studies suffer from small sample size coupled with high heterogeneity. They used this atlas to further dissect AML with t(8;21) (AML-ETO/RUNX1-RUNX1T1), which is one of the most frequent AML subtypes in young people. In particular, they were able to predict Gene Regulatory Networks in this AML subtype using pySCENIC, which identified the paediatric regulon defined by a distinct group of hematopoietic transcription factors (TFs) and the adult regulon for t(8;21). They further validated this in bulk RNA-seq with AUCell algorithm and inferred prenatal signature to 5 key TFs (KDM5A, REST, BCLAF1, YY1, and RAD21), and the postnatal signature to 9 TFs (ENO1, TFDP1, MYBL2, KLF1, TAGLN2, KLF2, IRF7, SPI1, and YXB1). They also used SCENIC+ to identify enhancer-driven regulons (eRegulons), forming an eGRN, and found that prenatal origin shows a specific HSC eRegulon profile, while a postnatal origin shows a GMP profile. They also did an in silico perturbation and found AP-1 complex (JUN, ATF4, FOSL2), P300, and BCLAF1 as important TFs to induce differentiation. Overall, I found this study very important in creating a comprehensive resource for AML research. 

Strengths: 

(1) The generation of an AML atlas integrating multiple datasets with almost 750K cells will further support the community working on AML. 

(2) Characterisation of t(8;21) AML proposes new interesting leads. 

We thank the reviewer for a succinct summary of our work and highlighting its strengths.

Weaknesses: 

Were these t(8;21) TFs/regulons identified from any of the single datasets? For example, if the authors apply pySCENIC to any dataset, would they find the same TFs, or is it the increase in the number of cells that allows identification of these? 

We implemented pySCENIC on individual datasets and compared the TFs (defining the regulons) identified to those from the combined AML scAtlas analysis. There were some common TFs identified, but these vary between individual studies. The union of all TFs identified makes a very large set - comprising around a third of all known TFs. AML scAtlas provides a more refined repertoire of TFs, perhaps as the underlying network inference approach is more robust with a higher number of cells. The findings of these investigations are included in Supplementary Figure 4DE, we hope this is useful for other users of pySCENIC.

Reviewer #2 (Public review): 

Summary: 

The authors assemble 222 publicly available bone marrow single-cell RNA sequencing samples from healthy donors and primary AML, including pediatric, adolescent, and adult patients at diagnosis. Focusing on one specific subtype, t(8;21), which, despite affecting all age classes, is associated with better prognosis and drug response for younger patients, the authors investigate if this difference is reflected also in the transcriptomic signal. Specifically, they hypothesize that the pediatric and part of the young population acquires leukemic mutations in utero, which leads to a different leukemogenic transformation and ultimately to differently regulated leukemic stem cells with respect to the adult counterpart. The analysis in this work heavily relies on regulatory network inference and clustering (via SCENIC tools), which identifies regulatory modules believed to distinguish the pre-, respectively, post-natal leukemic transformation. Bulk RNA-seq and scATAC-seq datasets displaying the same signatures are subsequently used for extending the pool of putative signature-specific TFs and enhancer elements. Through gene set enrichment, ontology, and perturbation simulation, the authors aim to interpret the regulatory signatures and translate them into potential onset-specific therapeutic targets. The putative pre-natal signature is associated with increased chemosensitivity, RNA splicing, histone modification, stemness marker SMARCA2, and potentially maintained by EP300 and BCLAF1. 

Strengths: 

The main strength of this work is the compilation of a pediatric AML atlas using the efficient Cellxgene interface. Also, the idea of identifying markers for different disease onsets, interpreting them from a developmental angle, and connecting this to the different therapy and relapse observations, is interesting. The results obtained, the set of putative up-regulated TFs, are biologically coherent with the mechanisms and the conclusions drawn. I also appreciate that the analysis code was made available and is well documented. 

We thank the reviewer for evaluating our work, and highlighting its key features, including creation of AML atlas, downstream analysis and interpretation for t(8;21) subtype.

Weaknesses:

There were fundamental flaws in how methods and samples were applied, a general lack of critical examination of both the results and the appropriateness of the methods for the data at hand, and in how results were presented. In particular: 

(1) Cell type annotation: 

(a) The 2-phase cell type annotation process employed for the scRNA-seq sample collection raised concerns. Initially annotated cells are re-labeled after a second round with the same cell types from the initial label pool (Figure 1E). The automatic annotation tools were used without specifying the database and tissue atlases used as a reference, and no information was shown regarding the consensus across these tools. 

Cell type annotations are heavily influenced by the reference profiles used and vary significantly between tools. To address this, we used multiple cell type annotation tools which predominantly encompassed healthy peripheral blood cell types and/or healthy bone marrow populations. This determined the primary cluster cell types assigned. 

Existing tools and resources are not leukemia specific, thus, to identify AMLassociated HSPC subpopulations we created a custom SingleR reference, using a CD34 enriched AML single-cell dataset. This was not suitable for the annotation of the full AML scAtlas, as it is derived from CD34 sorted cell types so is biased towards these populations. 

We have made this much clearer in the revised manuscript, by splitting Figure 1 into two separate figures (now Figure 1 and Figure 2) reflecting both different analyses performed. The methods have also been updated with more detail on the cell type annotations, and we have included the automated annotation outputs as a supplementary table, as this may be useful for others in the single-cell community. 

(b) Expression of the CD34 marker is only reported as a selection method for HSPCs, which is not in line with common practice. The use of only is admitted as a surface marker, while robust annotation of HSPCs should be done on the basis of expression of gene sets. 

Most of the cells used in the HSPC analysis were in fact annotated as HSPCs with some exceptions. In line with this feedback, we have re-worked this analysis and simply taken HSPC annotated clusters forward for the subsequent analysis, yielding the same findings. 

(c) During several analyses, the cell types used were either not well defined or contradictory, such as in Figure 2D, where it is not clear if pySCENIC and AUC scores were computed on HSPCs alone or merged with CMPs. In other cases, different cell type populations are compared and used interchangeably: comparing the HSPCderived regulons with bulk (probably not enriched for CD34+ cells) RNA samples could be an issue if there are no valid assumptions on the cell composition of the bulk sample. 

We apologize for the lack of clarity regarding which cell types were used, the text has been updated to clarify that in the pySCENIC analysis all myeloid progenitor cells were included. 

The bulk RNA-seq samples were used only to test the enrichment of our AML scAtlas derived regulons in an unbiased and large-scale way. While CD34 enriched samples could be preferable, this was not available to us. 

We agree that more effort could be made to ensure the single-cell/myeloid progenitor derived regulons are comparable to the bulk-RNA sequencing data. In the original bulk RNA-seq validation analysis, we used all bulk-RNA sequencing timepoints (diagnostic, on-treatment, relapse) and included both bone marrow and peripheral blood. Upon reflection, and to better harmonize the bulk RNA-seq selection strategy with that of AML scAtlas, we revised our approach to include only diagnostic bone marrow samples. We expect that, since the leukemia blast count for pediatric AML is typically high at diagnosis, these samples will predominantly contain leukemic blasts. 

(2) Method selection: 

(a) The authors should explain why they use pySCENIC and not any other approach.They should briefly explain how pySCENIC works and what they get out in the main text. In addition they should explain the AUCell algorithm and motivate its usage. 

pySCENIC is state-of-the-art method for network inference from scRNA data and is widely used within the single-cell community (over 5000 citations for both versions of the SCENIC pipeline). The pipeline has been benchmarked as one of the top performers for GRN analysis (Nguyen et al, 2021. Briefings in Bioinformatics). AUCELL is a module within the pySCENIC pipeline to summarize the activity of a set of genes (a regulon) into a single number which helps compare and visualize different regulons.  We have modified the manuscript (Results section 2 paragraph 2) to better explain this method and provided some rationale and accompanying citations to justify its use for this analysis. We thank the reviewer for highlighting this and hope our updates add some clarity.

(b) The obtained GRN signatures were not critically challenged on an external dataset. Therefore, the evidence that supports these signatures to be reliable and significant to the investigated setting is weak. 

These signatures were inferred using the most suitable AML single-cell RNA datasets currently available. To validate our findings, we used two independent datasets (the TARGET AML bulk RNA sequencing cohort, and the Lambo et al. scRNA-seq dataset). To clarify this workflow in the manuscript, we have added a panel to Figure 3 outlining the analytical process. To our knowledge, there are no other better-suited datasets for validation. Experimental validations on patient samples, while valuable, are beyond the scope of this study.

(3) There are some issues with the analysis & visualization of the data. 

Based on this feedback, we have improved several aspects of the analysis, changed some visualizations, and improved figure resolution throughout the manuscript. 

(4) Discussion: 

(a) What exactly is the 'regulon signature' that the authors infer? How can it be useful for insights into disease mechanisms? 

The ’regulon signature’ here refers to a gene regulatory program (multiple gene modules, each defined by a transcription factor and its targets) which are specific to different age groups. Further investigation into this can be useful for understanding why patients of different ages confer a different clinical course. We have amended the text to explain this.  

(b) The authors write 'Together this indicates that EP300 inhibition may be particularly effective in t(8;21) AML, and that BCLAF1 may present a new therapeutic target for t(8;21) AML, particularly in children with inferred pre-natal origin of the driver translocation.' I am missing a critical discussion of what is needed to further test the two targets. Put differently: Would the authors take the risk of a clinical study given the evidence from their analysis? 

Indeed, many extensive studies would be required before these findings are clinically translatable. We have included a discussion paragraph (discussion paragraph 7) detailing what further work is required in terms of experimental validation and potential subsequent clinical study.

Reviewer #1 (Recommendations for the authors): 

In addition to the point raised above, Cytoscape files for the GRNs and eGRNs inferred would be useful to have. 

We have now provided Cytoscape/eGRN tables in supplementary materials.

Reviewer #2 (Recommendations for the authors): 

(1) Figures 1F and 1G: You show the summed-up frequencies for all patients, right? It would be very interesting to see this per patient, or add error bars, since the shown frequencies might be driven by single patients with many cells. 

While this type of plot could be informative, the large number of samples in the AML scAtlas rendered the output difficult to interpret. As a result, we decided not to include it in the manuscript.

(2) An issue of selection bias has to be raised when only the two samples expressing the expected signatures are selected from the external scRNA dataset. Similarly, in the DepMap analysis, the age and nature of the other cell lines sensitive to EP300 and BCLAF1 should be reported. 

Since the purpose of this analysis was to build on previously defined signatures, we selected the two samples which we had preliminary hypotheses for. It would indeed be interesting to explore those not matching these signatures; however, samples numbers are very small, so without preliminary findings robust interpretation and validation would be difficult. An expanded validation would be more appropriate once more data becomes available in the future. 

We agree that investigating the age and nature of other BCLAF1/EP300 sensitive cell lines is a very valuable direction. Our analysis suggests that our BCLAF1 findings may also be applicable to other in-utero origin cancers, and we have now summarized these observations in Supplementary Figure 7H. 

(3) Is there statistical evidence for your claim that "This shows that higher-risk subtypes have a higher proportion of LSCs compared to favorable risk disease."? At least intermediate and adverse look similar to me. How does this look if you show single patients?  

We are grateful to the reviewer for noticing this oversight and have now included an appropriate statistical test in the revised manuscript. As before, while showing single patients may be useful, the large number of patients makes such plot difficult to interpret. For this reason, we have chosen not to include them.

(4) Specify the statistical test you used to 'identify significantly differentially expressed TFs' (line 192). 

The methods used for differential expression analysis are now clearly stated in the text as well as in the methods section. We hope this addition improves clarity for the reader.

(5) Figure 2B: You show the summed up frequencies for all patients, right? It would be intriguing to see this figure per patient, since the shown frequencies might be driven by single patients with many cells. 

Yes, the plot includes all patients. Showing individual patients on a single plot is not easily interpretable. 

(6) Y axis in 2D is not samples, but single cells? Please specify. 

We thank the reviewer for bringing this to our attention and have now updated Figure 3D accordingly. 

(7) Figure 3A: I don't get why the chosen clusters are designated as post- and prenatal, given the occurrence of samples in them. 

This figure serves to validate the previously defined regulon signatures, so the cluster designations are based on this. We have amended the text to elaborate on this point, which will hopefully provide greater clarity.

(8) Figure 3E: What is shown on the y axis? Did you correct your p-values for multiple testing? 

We apologize for this oversight and have now added a y axis label. P values were not corrected for multiple testing, as there are only few pairwise T tests performed.

(9) Robustness: You find some gene sets up- and down-regulated. How would that change if you used an eg bootstrapped number of samples, or a different analysis approach? 

To address this, we implemented both edgeR and DESeq2 for DE testing. Our findings (Supplementary Figure 5B) show that 98% of edgeR genes are also detected by DESeq2. We opted to use the smaller edgeR gene list for our analysis, due to the significant overlap showing robust findings. We thank the reviewer for this helpful suggestion, which has strengthened our analysis

(10) Multiomics analysis:

(a) Why only work on 'representative samples'? The idea of an integrated atlas is to identify robust patterns across patients, no? I'd love to see what regulons are robust, ie,  shared between patients.

As discussed in point 2, there are very few samples available for the multiomics analysis. Therefore, we chose to focus on those samples which we had a working hypothesis for, as a validation for our other analyses. 

(b) I don't agree that finding 'the key molecular processes, such as RNA splicing, histone modification, and TF binding' expressed 'further supports the stemness signature in presumed prenatal origin t(8;21) AML'.

Following the improvements made on the bulk RNA-Seq analysis in response to the previous reviewer comments, we ended up with a smaller gene set. Consequently, the ontology results have changed. The updated results are now more specific and indicate that developmental processes are upregulated in presumed prenatal origin t(8;21) AML. 

(c) Please clarify if the multiome data is part of the atlas.

The multiome data is not a part of AML scAtlas, as it was published at a later date. We used this dataset solely for validation purposes and have updated the figures and text to clearly indicate that it is used as a validation dataset.  

(d) Please describe the used data with respect to the number of patients, cells, age, etc.

We clarified this point in the text and have also included supplementary tables detailing all samples used in the atlas and validation datasets. 

(e) The four figures in Figure 4E look identical to me. What is the take-home message here? Do all perturbations have the same impact on driving differentiation? Please elaborate.

The perturbation figure is intended to illustrate that other genes can behave similarly to members of the AP-1 complex (JUN and ATF4 here) following perturbation. Since the AP-1 complex is well known to be important in t(8;21) AML, we hypothesize that these other genes are also important. We apologize for the previous lack of interpretation here and have amended the text to clarify this point. 

(11) Abstract: Please detail: how many of the 159 AML patients are t(8;21)? 

We have now amended the abstract to include this. 

(12) Figures: Increase font size where possible, eg age in 1B or risk group in 1G is super small and hard to read. 

Extra attention has been given to improving the figure readability and resolution throughout the whole manuscript.  

(13) Color codes in Figures 2B and 2C are all over the place and misleading: Sort 2C along age, indicate what is adult and adolescent, sort the x axis in 2B along age. 

We have changed this figure accordingly.  

(14) I suggest not coloring dendrograms, in my opinion this is highly irritating. 

The dendrogram colors correspond to clusters which are referenced in the text, this coloring provides informative context and aids interpretation, making it a useful addition to the figure.

(15) The resolution in Figure 4B is bad, I can't read the labels. 

This visualization has been revised, to make presentation of this data clearer.  

(16) In addition to selecting bulk RNA samples matching the two regulon signatures, some effort should have been put into investigating the samples not aligned with those, or assessing how unique these GRN signatures are to the specific cell type and disease of interest, excluding the influence of cell type composition and random noise. The lateonset signatures should also be excluded from being present in an external pre-natal cohort in a more statistically rigorous manner. 

Our use of the bulk RNA-Seq data is solely intended for the validation of predefined regulon signatures, for which we already have a working hypothesis.  While we agree that further investigation of the samples that do not align with these signatures could yield interesting insights, we believe that such an analysis would extend beyond the scope of the current manuscript.

(17) The specific bulk RNA samples used should be specified, along with the tissue of origin. The same goes for the Lambo dataset. 

We have clarified this point in the text and provided a supplementary table detailing all samples used for validation, alongside the sample list from AML scAtlas.

(18) In Supplementary Figure 5 B, the axes should be define. 

We have updated this figure to include axis legends.

(19) Supplementary Figure 4A. There is a mistake in the sex assignment for sample AML14D. Since chrY-genes are expressed, this sample is likely male, while the Xist expression is mostly zero. 

We thank the reviewer for pointing out this error, which has now been corrected.  

(20) Wording suggestions: 

(a) Line 54: not compelling phrasing. 

(b) Line 83: "allows to decipher". 

(c) Line 88: repetition from line 85. 

(d) Line 90: the expression "clean GRN" is not clear. 

These wording suggestions have all been incorporated in the revised manuscript.

(21) Supplementary Figure 3D is not interpretable, I suggest a different visualization. 

We agree that the original figure was not the most informative and have replaced it with UMAPs displaying LSC6 and LSC17 scores.

eLife Assessment

The use of DNA tethers is an important advance for studying how motor proteins respond to load. The authors use a convincing methodology to investigate the detachment and reattachment kinetics of kinesin-1, 2, and 3 motors against loads oriented parallel to the microtubule. As the manuscript stands, the conclusions drawn from the experiments, as well as the overall interpretation of the results, are incompletely supported by the presented data, and the novelty over previous reports appears less clear.

Reviewer #1 (Public review):

Summary:

Noell et al have presented a careful study of the dissociation kinetics of Kinesin (1,2,3) classes of motors moving in vitro on a microtubule. These motors move against the opposing force from a ~1 micron DNA strand (DNA tensiometer) that is tethered to the microtubule and also bound to the motor via specific linkages (Figure 1A). The authors compare the time for which motors remain attached to the microtubule when they are tethered to the DNA, versus when they are not. If the former is longer, the interpretation is that the force on the motor from the stretched DNA (presumed to be working solely along the length of the microtubule) causes the motor's detachment rate from the microtubule to be reduced. Thus, the specific motor exhibits "catch-bond" like behaviour.

Strengths:

The motivation is good - to understand how kinesin competes against dynein through the possible activation of a catch bond. Experiments are well done, and there is an effort to model the results theoretically.

Weaknesses:

The motivation of these studies is to understand how kinesin (1/2/3) motors would behave when they are pitted in a tug of war against dynein motors as they transport cargo in a bidirectional manner on microtubules. Earlier work on dynein and kinesin motors using optical tweezers has suggested that dynein shows a catch bond phenomenon, whereas such signatures were not seen for kinesin. Based on their data with the DNA tensiometer, the authors would like to claim that (i) Kinesin1 and Kinesin2 also show catch-bonding and (ii) the earlier results using optical traps suffer from vertical forces, which complicates the catch-bond interpretation.

While the motivation of this work is reasonable, and the experiments are careful, I find significant issues that the authors have not addressed:

(1) Figure 1B shows the PREDICTED force-extension curve for DNA based on a worm-like chain model. Where is the experimental evidence for this curve? This issue is crucial because the F-E curve will decide how and when a catch-bond is induced (if at all it is) as the motor moves against the tensiometer. Unless this is actually measured by some other means, I find it hard to accept all the results based on Figure 1B.

(2) The authors can correct me on this, but I believe that all the catch-bond studies using optical traps have exerted a load force that exceeds the actual force generated by the motor. For example, see Figure 2 in reference 42 (Kunwar et al). It is in this regime (load force > force from motor) that the dissociation rate is reduced (catch-bond is activated). Such a regime is never reached in the DNA tensiometer study because of the very construction of the experiment. I am very surprised that this point is overlooked in this manuscript. I am therefore not even sure that the present experiments even induce a catch-bond (in the sense reported for earlier papers).

(3) I appreciate the concerns about the Vertical force from the optical trap. But that leads to the following questions that have not at all been addressed in this paper:

(i) Why is the Vertical force only a problem for Kinesins, and not a problem for the dynein studies?

(ii) The authors state that "With this geometry, a kinesin motor pulls against the elastic force of a stretched DNA solely in a direction parallel to the microtubule". Is this really true? What matters is not just how the kinesin pulls the DNA, but also how the DNA pulls on the kinesin. In Figure 1A, what is the guarantee that the DNA is oriented only in the plane of the paper? In fact, the DNA could even be bending transiently in a manner that it pulls the kinesin motor UPWARDS (Vertical force). How are the authors sure that the reaction force between DNA and kinesin is oriented SOLELY along the microtubule?

(4) For this study to be really impactful and for some of the above concerns to be addressed, the data should also have included DNA tensiometer experiments with Dynein. I wonder why this was not done?

While I do like several aspects of the paper, I do not believe that the conclusions are supported by the data presented in this paper for the reasons stated above.

Reviewer #2 (Public review):

Summary:

To investigate the detachment and reattachment kinetics of kinesin-1, 2, and 3 motors against loads oriented parallel to the microtubule, the authors used a DNA tensiometer approach comprising a DNA entropic spring attached to the microtubule on one end and a motor on the other. They found that for kinesin-1 and kinesin-2, the dissociation rates at stall were smaller than the detachment rates during unloaded runs. With regard to the complex reattachment kinetics found in the experiments, the authors argue that these findings were consistent with a weakly-bound 'slip' state preceding motor dissociation from the microtubule. The behavior of kinesin-3 was different and (by the definition of the authors) only showed prolonged "detachment" rates when disregarding some of the slip events. The authors performed stochastic simulations that recapitulate the load-dependent detachment and reattachment kinetics for all three motors. They argue that the presented results provide insight into how kinesin-1, -2, and -3 families transport cargo in complex cellular geometries and compete against dynein during bidirectional transport.

Strengths:

The present study is timely, as significant concerns have been raised previously about studying motor kinetics in optical (single-bead) traps where significant vertical forces are present. Moreover, the obtained data are of high quality, and the experimental procedures are clearly described.

Weaknesses:

However, in the present version of the manuscript, the conclusions drawn from the experiments, the overall interpretation of the results, and the novelty over previous reports appear less clear.

Major comments:

(1) The use of the term "catch bond" is misleading, as the authors do not really mean consistently a catch bond in the classical sense (i.e., a protein-protein interaction having a dissociation rate that decreases with load). Instead, what they mean is that after motor detachment (i.e., after a motor protein dissociating from a tubulin protein), there is a slip state during which the reattachment rate is higher as compared to a motor diffusing in solution. While this may indeed influence the dynamics of bidirectional cargo transport (e.g., during tug-of-war events), the used terms (detachment (with or without slip?), dissociation, rescue, ...) need to be better defined and the results discussed in the context of these definitions. It is very unsatisfactory at the moment, for example, that kinesin-3 is at first not classified as a catch bond, but later on (after tweaking the definitions) it is. In essence, the typical slip/catch bond nomenclature used for protein-protein interaction is not readily applicable for motors with slippage.

(2) The authors define the stall duration as the time at full load, terminated by >60 nm slips/detachments. Isn't that a problem? Smaller slips are not detected/considered... but are also indicative of a motor dissociation event, i.e., the end of a stall. What is the distribution of the slip distances? If the slip distances follow an exponential decay, a large number of short slips are expected, and the presented data (neglecting those short slips) would be highly distorted.

(3) Along the same line: Why do the authors compare the stall duration (without including the time it took the motor to reach stall) to the unloaded single motor run durations? Shouldn't the times of the runs be included?

(4) At many places, it appears too simple that for the biologically relevant processes, mainly/only the load-dependent off-rates of the motors matter. The stall forces and the kind of motor-cargo linkage (e.g., rigid vs. diffusive) do likely also matter. For example: "In the context of pulling a large cargo through the viscous cytoplasm or competing against dynein in a tug-of-war, these slip events enable the motor to maintain force generation and, hence, are distinct from true detachment events." I disagree. The kinesin force at reattachment (after slippage) is much smaller than at stall. What helps, however, is that due to the geometry of being held close to the microtubule (either by the DNA in the present case or by the cargo in vivo) the attachment rate is much higher. Note also that upon DNA relaxation ,the motor is likely kept close to the microtubule surface, while, for example, when bound to a vesicle, the motor may diffuse away from the microtubule quickly (e.g., reference 20).

(5) Why were all motors linked to the neck-coil domain of kinesin-1? Couldn't it be that for normal function, the different coils matter? Autoinhibition can also be circumvented by consistently shortening the constructs.

(6) I am worried about the neutravidin on the microtubules, which may act as roadblocks (e.g. DOI: 10.1039/b803585g), slip termination sites (maybe without the neutravidin, the rescue rate would be much lower?), and potentially also DNA-interaction sites? At 8 nM neutravidin and the given level of biotinylation, what density of neutravidin do the authors expect on their microtubules? Can the authors rule out that the observed stall events are predominantly the result of a kinesin motor being stopped after a short slippage event at a neutravidin molecule?

(7) Also, the unloaded runs should be performed on the same microtubules as in the DNA experiments, i.e., with neutravidin. Otherwise, I do not see how the values can be compared.

(8) If, as stated, "a portion of kinesin-3 unloaded run durations were limited by the length of the microtubules, meaning the unloaded duration is a lower limit." corrections (such as Kaplan-Meier) should be applied, DOI: 10.1016/j.bpj.2017.09.024.

(9) Shouldn't Kaplan-Meier also be applied to the ramp durations ... as a ramp may also artificially end upon stall? Also, doesn't the comparison between ramp and stall duration have a problem, as each stall is preceded by a ramp ...and the (maximum) ramp times will depend on the speed of the motor? Kinesin-3 is the fastest motor and will reach stall much faster than kinesin-1. Isn't it obvious that the stall durations are longer than the ramp duration (as seen for all three motors in Figure 3)?

(10) It is not clear what is seen in Figure S6A: It looks like only single motors (green, w/o a DNA molecule) are walking ... Note: the influence of the attached DNA onto the stepping duration of a motor may depend on the DNA conformation (stretched and near to the microtubule (with neutravidin!) in the tethered case and spherically coiled in the untethered case).

(11) Along this line: While the run time of kinesin-1 with DNA (1.4 s) is significantly shorter than the stall time (3.0 s), it is still larger than the unloaded run time (1.0 s). What do the authors think is the origin of this increase?

(12) "The simplest prediction is that against the low loads experienced during ramps, the detachment rate should match the unloaded detachment rate." I disagree. I would already expect a slight increase.

(13) Isn't the model over-defined by fitting the values for the load-dependence of the strong-to-weak transition and fitting the load dependence into the transition to the slip state?

(14) "When kinesin-1 was tethered to a glass coverslip via a DNA linker and hydrodynamic forces were imposed on an associated microtubule, kinesin-1 dissociation rates were relatively insensitive to loads up to ~3 pN, inconsistent with slip-bond characteristics (37)." This statement appears not to be true. In reference 37, very similar to the geometry reported here, the microtubules were fixed on the surface, and the stepping of single kinesin motors attached to large beads (to which defined forces were applied by hydrodynamics) via long DNA linkers was studied. In fact, quite a number of statements made in the present manuscript have been made already in ref. 37 (see in particular sections 2.6 and 2.7), and the authors may consider putting their results better into this context in the Introduction and Discussion. It is also noteworthy to discuss that the (admittedly limited) data in ref. 37 does not indicate a "catch-bond" behavior but rather an insensitivity to force over a defined range of forces.

Reviewer #3 (Public review):

Summary:

Several recent findings indicate that forces perpendicular to the microtubule accelerate kinesin unbinding, where perpendicular and axial forces were analyzed using the geometry in a single-bead optical trapping assay (Khataee and Howard, 2019), comparison between single-bead and dumbbell assay measurements (Pyrpassopoulos et al., 2020), and comparison of single-bead optical trap measurements with and without a DNA tether (Hensley and Yildiz, 2025).

Here, the authors devise an assay to exert forces along the microtubule axis by tethering kinesin to the microtubule via a dsDNA tether. They compared the behavior of kinesin-1, -2, and -3 when pulling against the DNA tether. In line with previous optical trapping measurements, kinesin unbinding is less sensitive to forces when the forces are aligned with the microtubule axis. Surprisingly, the authors find that both kinesin-1 and -2 detach from the microtubule more slowly when stalled against the DNA tether than in unloaded conditions, indicating that these motors act as catch bonds in response to axial loads. Axial loads accelerate kinesin-3 detachment. However, kinesin-3 reattaches quickly to maintain forces. For all three kinesins, the authors observe weakly attached states where the motor briefly slips along the microtubule before continuing a processive run.

Strengths:

These observations suggest that the conventional view that kinesins act as slip bonds under load, as concluded from single-bead optical trapping measurements where perpendicular loads are present due to the force being exerted on the centroid of a large (relative to the kinesin) bead, needs to be reconsidered. Understanding the effect of force on the association kinetics of kinesin has important implications for intracellular transport, where the force-dependent detachment governs how kinesins interact with other kinesins and opposing dynein motors (Muller et al., 2008; Kunwar et al., 2011; Ohashi et al., 2018; Gicking et al., 2022) on vesicular cargoes.

Weaknesses:

The authors attribute the differences in the behaviour of kinesins when pulling against a DNA tether compared to an optical trap to the differences in the perpendicular forces. However, the compliance is also much different in these two experiments. The optical trap acts like a ~ linear spring with stiffness ~ 0.05 pN/nm. The dsDNA tether is an entropic spring, with negligible stiffness at low extensions and very high compliance once the tether is extended to its contour length (Fig. 1B). The effect of the compliance on the results should be addressed in the manuscript.

Compared to an optical trapping assay, the motors are also tethered closer to the microtubule in this geometry. In an optical trap assay, the bead could rotate when the kinesin is not bound. The authors should discuss how this tethering is expected to affect the kinesin reattachment and slipping. While likely outside the scope of this study, it would be interesting to compare the static tether used here with a dynamic tether like MAP7 or the CAP-GLY domain of p150glued.

In the single-molecule extension traces (Figure 1F-H; S3), the kinesin-2 traces often show jumps in position at the beginning of runs (e.g., the four runs from ~4-13 s in Fig. 1G). These jumps are not apparent in the kinesin-1 and -3 traces. What is the explanation? Is kinesin-2 binding accelerated by resisting loads more strongly than kinesin-1 and -3?

When comparing the durations of unloaded and stall events (Fig. 2), there is a potential for bias in the measurement, where very long unloaded runs cannot be observed due to the limited length of the microtubule (Thompson, Hoeprich, and Berger, 2013), while the duration of tethered runs is only limited by photobleaching. Was the possible censoring of the results addressed in the analysis?

The mathematical model is helpful in interpreting the data. To assess how the "slip" state contributes to the association kinetics, it would be helpful to compare the proposed model with a similar model with no slip state. Could the slips be explained by fast reattachments from the detached state?

Author response:

Reviewer 1 (Public review):

(1) Figure 1B shows the PREDICTED force-extension curve for DNA based on a worm-like chain model. Where is the experimental evidence for this curve? This issue is crucial because the F-E curve will decide how and when a catch-bond is induced (if at all it is) as the motor moves against the tensiometer. Unless this is actually measured by some other means, I find it hard to accept all the results based on Figure 1B.

The Worm-Like-Chain model for the elasticity of DNA was established by early work from the Bustamante lab (Smith et al., 1992)  and Marko and Siggia (Marko and Siggia, 1995), and was further validated and refined by the Block lab (Bouchiat et al., 1999; Wang et al., 1997). The 50 nm persistence length is the consensus value, and was shown to be independent of force and extension in Figure 3 of Bouchiat et al (Bouchiat et al., 1999). However, we would like to stress that for our conclusions, the precise details of the Force-Extension relationship of our dsDNA are immaterial. The key point is that the motor stretches the DNA and stalls when it reaches its stall force. Our claim of the catch-bond character of kinesin is based on the longer duration at stall compared to the run duration in the absence of load. Provided that the motor is indeed stalling because it has stretched out the DNA (which is strongly supported by the repeated stalling around the predicted extension corresponding to ~6 pN of force), then the stall duration depends on neither the precise value for the extension nor the precise value of the force at stall.

(2) The authors can correct me on this, but I believe that all the catch-bond studies using optical traps have exerted a load force that exceeds the actual force generated by the motor. For example, see Figure 2 in reference 42 (Kunwar et al). It is in this regime (load force > force from motor) that the dissociation rate is reduced (catch-bond is activated). Such a regime is never reached in the DNA tensiometer study because of the very construction of the experiment. I am very surprised that this point is overlooked in this manuscript. I am therefore not even sure that the present experiments even induce a catch-bond (in the sense reported for earlier papers).

It is true that Kunwar et al measured binding durations at super-stall loads and used that to conclude that dynein does act as a catch-bond (but kinesin does not) (Kunwar et al., 2011). However, we would like to correct the reviewer on this one. This approach of exerting super-stall forces and measuring binding durations is in fact less common than the approach of allowing the motor to walk up to stall and measuring the binding duration. This ‘fixed trap’ approach has been used to show catch-bond behavior of dynein (Leidel et al., 2012; Rai et al., 2013) and kinesin (Kuo et al., 2022; Pyrpassopoulos et al., 2020). For the non-processive motor Myosin I, a dynamic force clamp was used to keep the actin filament in place while the myosin generated a single step (Laakso et al., 2008). Because the motor generates the force, these are not superstall forces either.

(3) I appreciate the concerns about the Vertical force from the optical trap. But that leads to the following questions that have not at all been addressed in this paper:

(i) Why is the Vertical force only a problem for Kinesins, and not a problem for the dynein studies?

Actually, we do not claim that vertical force is not a problem for dynein; our data do not speak to this question. There is debate in the literature as to whether dynein has catch bond behavior in the traditional single-bead optical trap geometry - while some studies have measured dynein catch bond behavior (Kunwar et al., 2011; Leidel et al., 2012; Rai et al., 2013), others have found that dynein has slip-bond or ideal-bond behavior (Ezber et al., 2020; Nicholas et al., 2015; Rao et al., 2019). This discrepancy may relate to vertical forces, but not in an obvious way.

(ii) The authors state that "With this geometry, a kinesin motor pulls against the elastic force of a stretched DNA solely in a direction parallel to the microtubule". Is this really true? What matters is not just how the kinesin pulls the DNA, but also how the DNA pulls on the kinesin. In Figure 1A, what is the guarantee that the DNA is oriented only in the plane of the paper? In fact, the DNA could even be bending transiently in a manner that it pulls the kinesin motor UPWARDS (Vertical force). How are the authors sure that the reaction force between DNA and kinesin is oriented SOLELY along the microtubule?

We acknowledge that “solely” is an absolute term that is too strong to describe our geometry. We will soften this term in our revision to “nearly parallel to the microtubule”. In the Geometry Calculations section of Supplementary Methods, we calculate that if the motor and streptavidin are on the same protofilament, the vertical force will be <1% of the horizontal force. We also note that if the motor is on a different protofilament, there will be lateral forces and forces perpendicular to the microtubule surface, except they are oriented toward rather than away from the microtubule. The DNA can surely bend due to thermal forces, but because inertia plays a negligible role at the nanoscale (Howard, 2001; Purcell, 1977), any resulting upward forces will only be thermal forces, which the motor is already subjected to at all times.

(4) For this study to be really impactful and for some of the above concerns to be addressed, the data should also have included DNA tensiometer experiments with Dynein. I wonder why this was not done?

As much as we would love to fully characterize dynein here, this paper is about kinesin and it took a substantial effort. The dynein work merits a stand-alone paper.

While I do like several aspects of the paper, I do not believe that the conclusions are supported by the data presented in this paper for the reasons stated above.

The three key points the reviewer makes are the validity of the worm-like-chain model, the question of superstall loads, and the role of DNA bending in generating vertical forces. We hope that we have fully addressed these concerns in our responses above.

Reviewer #2 (Public review):

Major comments:

(1) The use of the term "catch bond" is misleading, as the authors do not really mean consistently a catch bond in the classical sense (i.e., a protein-protein interaction having a dissociation rate that decreases with load). Instead, what they mean is that after motor detachment (i.e., after a motor protein dissociating from a tubulin protein), there is a slip state during which the reattachment rate is higher as compared to a motor diffusing in solution. While this may indeed influence the dynamics of bidirectional cargo transport (e.g., during tug-of-war events), the used terms (detachment (with or without slip?), dissociation, rescue, ...) need to be better defined and the results discussed in the context of these definitions. It is very unsatisfactory at the moment, for example, that kinesin-3 is at first not classified as a catch bond, but later on (after tweaking the definitions) it is. In essence, the typical slip/catch bond nomenclature used for protein-protein interaction is not readily applicable for motors with slippage.

We appreciate the reviewer’s point and we will work to streamline and define terms in our revision.

(2) The authors define the stall duration as the time at full load, terminated by >60 nm slips/detachments. Isn't that a problem? Smaller slips are not detected/considered... but are also indicative of a motor dissociation event, i.e., the end of a stall. What is the distribution of the slip distances? If the slip distances follow an exponential decay, a large number of short slips are expected, and the presented data (neglecting those short slips) would be highly distorted.

The reviewer brings up a good point that there may be undetected slips. To address this question, we plotted the distribution of slip distances for kinesin-3, which by far had the most slip events. As the reviewer suggested, it is indeed an exponential distribution. Our preliminary analysis suggests that roughly 20% of events are missed due to this 60 nm cutoff. This will change our unloaded duration numbers slightly, but this will not alter our conclusions.\

(3) Along the same line: Why do the authors compare the stall duration (without including the time it took the motor to reach stall) to the unloaded single motor run durations? Shouldn't the times of the runs be included?

The elastic force of the DNA spring is variable as the motor steps up to stall, and so if we included the entire run duration then it would be difficult to specify what force we were comparing to unloaded. More importantly, if we assume that any stepping and detachment behavior is history independent, then it is mathematically proper to take any arbitrary starting point (such as when the motor reaches stall), start the clock there, and measure the distribution of detachments durations relative to that starting point.

More importantly, what we do in Fig. 3 is to separate out the ramps from the stalls and, using a statistical model, we compute a separate duration parameter (which is the inverse of the off-rate) for the ramp and the stall. What we find is that the relationship between ramp, stall, and unloaded durations is different for the three motors, which is interesting in itself.

(4) At many places, it appears too simple that for the biologically relevant processes, mainly/only the load-dependent off-rates of the motors matter. The stall forces and the kind of motor-cargo linkage (e.g., rigid vs. diffusive) do likely also matter. For example: "In the context of pulling a large cargo through the viscous cytoplasm or competing against dynein in a tug-of-war, these slip events enable the motor to maintain force generation and, hence, are distinct from true detachment events." I disagree. The kinesin force at reattachment (after slippage) is much smaller than at stall. What helps, however, is that due to the geometry of being held close to the microtubule (either by the DNA in the present case or by the cargo in vivo) the attachment rate is much higher. Note also that upon DNA relaxation, the motor is likely kept close to the microtubule surface, while, for example, when bound to a vesicle, the motor may diffuse away from the microtubule quickly (e.g., reference 20).

We appreciate the reviewer’s detailed thinking here, and we offer our perspective. As to the first point, we agree that the stall force is relevant and that the rigidity of the motor-cargo linkage will play a role. The goal of the sentence on pulling cargo that the reviewer highlights is to set up our analysis of slips, which we define as rearward displacements that don’t return to the baseline before force generation resumes. We agree that force after slippage is much smaller than at stall, and we plan to clarify that section of text. However, as shown in the model diagram in Fig. 5, we differentiate between the slip state (and recovery from this slip state) and the detached state (and reattachment from this detached state). This delineation is important because, as the reviewer points out, if we are measuring detachment and reattachment with our DNA tensiometer, then the geometry of a vesicle in a cell will be different and diffusion away from the microtubule or elastic recoil perpendicular to the microtubule will suppress this reattachment.

Our evidence for a slip state in which the motor maintains association with the microtubule comes from optical trapping work by Tokelis et al (Toleikis et al., 2020) and Sudhakar et al (Sudhakar et al., 2021). In particular, Sudhakar used small, high index Germanium microspheres that had a low drag coefficient. They showed that during ‘slip’ events, the relaxation time constant of the bead back to the center of the trap was nearly 10-fold slower than the trap response time, consistent with the motor exerting drag on the microtubule. (With larger beads, the drag of the bead swamps the motor-microtubule friction.) Another piece of support for the motor maintaining association during a slip is work by Ramaiya et al. who used birefringent microspheres to exert and measure rotational torque during kinesin stepping (Ramaiya et al., 2017). In most traces, when the motor returned to baseline following a stall, the torque was dissipated as well, consistent with a ‘detached’ state. However, a slip event is shown in S18a where the motor slips backward while maintaining torque. This is best explained by the motor slipping backward in a state where the heads are associated with the microtubule (at least sufficiently to resist rotational forces). Thus, we term the resumption after slip to be a rescue from the slip state rather than a reattachment from the detached state.

To finish the point, with the complex geometry of a vesicle, during slip events the motor remains associated with the microtubule and hence primed for recovery. This recovery rate is expected to be the same as for the DNA tensiometer. Following a detachment, however, we agree that there will likely be a higher probability of reattachment in the DNA tensiometer due to proximity effects, whereas with a vesicle any elastic recoil or ‘rolling’ will pull the detached motor away from the microtubule, suppressing reattachment. We plan to clarify these points in the text of the revision.

(5) Why were all motors linked to the neck-coil domain of kinesin-1? Couldn't it be that for normal function, the different coils matter? Autoinhibition can also be circumvented by consistently shortening the constructs.

We chose this dimerization approach to focus on how the mechoanochemical properties of kinesins vary between the three dominant transport families. We agree that in cells, autoinhibition of both kinesins and dynein likely play roles in regulating bidirectional transport, as will the activity of other regulatory proteins. The native coiled-coils may act as as ‘shock absorbers’ due to their compliance, or they might slow the motor reattachment rate due to the relatively large search volumes created by their long lengths (10s of nm). These are topics for future work. By using the neck-coil domain of kinesin-1 for all three motors, we eliminate any differences in autoinhibition or other regulation between the three kinesin families and focus solely on differences in the mechanochemistry of their motor domains.

(6) I am worried about the neutravidin on the microtubules, which may act as roadblocks (e.g. DOI: 10.1039/b803585g), slip termination sites (maybe without the neutravidin, the rescue rate would be much lower?), and potentially also DNA-interaction sites? At 8 nM neutravidin and the given level of biotinylation, what density of neutravidin do the authors expect on their microtubules? Can the authors rule out that the observed stall events are predominantly the result of a kinesin motor being stopped after a short slippage event at a neutravidin molecule?

We will address these points in our revision.

(7) Also, the unloaded runs should be performed on the same microtubules as in the DNA experiments, i.e., with neutravidin. Otherwise, I do not see how the values can be compared.

We will address this point in our revision.

(8) If, as stated, "a portion of kinesin-3 unloaded run durations were limited by the length of the microtubules, meaning the unloaded duration is a lower limit." corrections (such as Kaplan-Meier) should be applied, DOI: 10.1016/j.bpj.2017.09.024.

(9) Shouldn't Kaplan-Meier also be applied to the ramp durations ... as a ramp may also artificially end upon stall? Also, doesn't the comparison between ramp and stall duration have a problem, as each stall is preceded by a ramp ...and the (maximum) ramp times will depend on the speed of the motor? Kinesin-3 is the fastest motor and will reach stall much faster than kinesin-1. Isn't it obvious that the stall durations are longer than the ramp duration (as seen for all three motors in Figure 3)?

The reviewer rightly notes the many challenges in estimating the motor off-rates during ramps. To estimate ramp off-rates and as an independent approach to calculating the unloaded and stall durations, we developed a Markov model coupled with Bayesian inference methods to estimate a duration parameter (equivalent to the inverse of the off-rate) for the unloaded, ramp, and stall duration distributions. With the ramps, we have left censoring due to the difficulty in detecting the start of the ramps in the fluctuating baseline, and we have right censoring due to reaching stall (with different censoring of the ramp duration for the three motors due to their different speeds). The Markov model assumes a constant detachment probability and history independence, and thus is robust even in the face of left and right censoring (details in the Supplementary section). This approach is preferred over Kaplan-Meier because, although these non-parametric methods make no assumptions for the distribution, they require the user to know exactly where the start time is.

Regarding the potential underestimate of the kinesin-3 unloaded run duration due to finite microtubule lengths. The first point is that the unloaded duration data in Fig. 2C are quite linear up to 6 s and are well fit by the single-exponential fit (the points above 6s don’t affect the fit very much). The second point is that when we used our Markov model (which is robust against right censoring) to estimate the unloaded and stall durations, the results agreed with the single-exponential fits very well (Table S2). For instance, the single-exponential fit for the kinesin-3 unloaded duration was 2.74 s (2.33 – 3.17 s 95% CI) and the estimate from the Markov model was 2.76 (2.28 – 3.34 s 95% CI). Thus, we chose not to make any corrections due to finite microtubule lengths.

(10) It is not clear what is seen in Figure S6A: It looks like only single motors (green, w/o a DNA molecule) are walking ... Note: the influence of the attached DNA onto the stepping duration of a motor may depend on the DNA conformation (stretched and near to the microtubule (with neutravidin!) in the tethered case and spherically coiled in the untethered case).

In Figure S6A kymograph, the green traces are GFP-labeled kinesin-1 without DNA attached (which are in excess) and the red diagonal trace is a motor with DNA attached. There are also two faint horizontal red traces, which are labeled DNA diffusing by (smearing over a large area during a single frame). Panel S6B shows run durations of motors with DNA attached. We agree that the DNA conformation will differ if it is attached and stretched (more linear) versus simply being transported (random coil), but by its nature this control experiment is only addressing random coil DNA.

(11) Along this line: While the run time of kinesin-1 with DNA (1.4 s) is significantly shorter than the stall time (3.0 s), it is still larger than the unloaded run time (1.0 s). What do the authors think is the origin of this increase?

Our interpretation of the unloaded kinesin-DNA result is that the much slower diffusion constant of the DNA relative to the motor alone enables motors to transiently detach and rebind before the DNA cargo has diffused away, thus extending the run duration. In contrast, such detachment events for motors alone normally result in the motor diffusing away from the microtubule, terminating the run. This argument has been used to reconcile the longer single-motor run lengths in the gliding assay versus the bead assay (Block et al., 1990). Notably, this slower diffusion constant should not play a role in the DNA tensiometer geometry because if the motor transiently detaches, then it will be pulled backward by the elastic forces of the DNA and detected as a slip or detachment event. We will address this point in the revision.

(12) "The simplest prediction is that against the low loads experienced during ramps, the detachment rate should match the unloaded detachment rate." I disagree. I would already expect a slight increase.

Agreed. We will change this text to: “The prediction for a slip bond is that against the low loads experienced during ramps, the detachment rate should be equal to or faster than the unloaded detachment rate.”

(13) Isn't the model over-defined by fitting the values for the load-dependence of the strong-to-weak transition and fitting the load dependence into the transition to the slip state?

Essentially, yes, it is overdefined, but that is essentially by design and it is still very useful. Our goal here was to make as simple a model as possible that could account for the data and use it to compare model parameters for the different motor families. Ignoring the complexity of the slip and detached states, a model with a strong and weak state in the stepping cycle and a single transition out of the stepping cycle is the simplest formulation possible. And having rate constants (k_S-W and k_slip in our case) that vary exponentially with load makes thermodynamic sense for modeling mechanochemistry (Howard, 2001). Thus, we were pleasantly surprised that this bare-bones model could recapitulate the unloaded and stall durations for all three motors (Fig. 5C-E).

(14) "When kinesin-1 was tethered to a glass coverslip via a DNA linker and hydrodynamic forces were imposed on an associated microtubule, kinesin-1 dissociation rates were relatively insensitive to loads up to ~3 pN, inconsistent with slip-bond characteristics (37)." This statement appears not to be true. In reference 37, very similar to the geometry reported here, the microtubules were fixed on the surface, and the stepping of single kinesin motors attached to large beads (to which defined forces were applied by hydrodynamics) via long DNA linkers was studied. In fact, quite a number of statements made in the present manuscript have been made already in ref. 37 (see in particular sections 2.6 and 2.7), and the authors may consider putting their results better into this context in the Introduction and Discussion. It is also noteworthy to discuss that the (admittedly limited) data in ref. 37 does not indicate a "catch-bond" behavior but rather an insensitivity to force over a defined range of forces.

The reviewer misquoted our sentence. The actual wording of the sentence was: “When kinesin-1 was connected to micron-scale beads through a DNA linker and hydrodynamic forces parallel to the microtubule imposed, dissociation rates were relatively insensitive to loads up to ~3 pN, inconsistent with slip-bond characteristics (Urbanska et al., 2021).” The sentence the reviewer quoted was in a previous version that is available on BioRxiv and perhaps they were reading that version. Nonetheless, in the revision we will note in the Discussion that this behavior was indicative of an ideal bond (not a catch-bond), and we will also add a sentence in the Introduction highlighting this work.

Reviewer #3 (Public review):

The authors attribute the differences in the behaviour of kinesins when pulling against a DNA tether compared to an optical trap to the differences in the perpendicular forces. However, the compliance is also much different in these two experiments. The optical trap acts like a ~ linear spring with stiffness ~ 0.05 pN/nm. The dsDNA tether is an entropic spring, with negligible stiffness at low extensions and very high compliance once the tether is extended to its contour length (Fig. 1B). The effect of the compliance on the results should be addressed in the manuscript.

This is an interesting point. To address it, we calculated the predicted stiffness of the dsDNA by taking the slope of theoretical force-extension curve in Fig. 1B. Below 650 nm extension, the stiffness is <0.001 pN/nM; it reaches 0.01 pN/nM at 855 nm, and at 960 nm where the force is 6 pN the stiffness is roughly 0.2 pN/nm. That value is higher than the quoted 0.05 pN/nm trap stiffness, but for reference, at this stiffness, an 8 nm step leads to a 1.6 pN jump in force, which is reasonable. Importantly, the stiffness of kinesin motors has been estimated to be in the range of 0.3 pN (Coppin et al., 1996; Coppin et al., 1997). Granted, this stiffness is also nonlinear, but what this means is that even at stall, our dsDNA tether has a similar predicted compliance to the motor that is pulling on it. We will address this point in our revision.  

Compared to an optical trapping assay, the motors are also tethered closer to the microtubule in this geometry. In an optical trap assay, the bead could rotate when the kinesin is not bound. The authors should discuss how this tethering is expected to affect the kinesin reattachment and slipping. While likely outside the scope of this study, it would be interesting to compare the static tether used here with a dynamic tether like MAP7 or the CAP-GLY domain of p150glued.

Please see our response to Reviewer #2 Major Comment #4 above, which asks this same question in the context of intracellular cargo. We plan to address this in our revision. Regarding a dynamic tether, we agree that’s interesting – there are kinesins that have a second, non-canonical binding site that achieves this tethering (ncd and Cin8); p150glued likely does this naturally for dynein-dynactin-activator complexes; and we speculated in a review some years ago (Hancock, 2014) that during bidirectional transport kinesin and dynein may act as dynamic tethers for one another when not engaged, enhancing the activity of the opposing motor.

In the single-molecule extension traces (Figure 1F-H; S3), the kinesin-2 traces often show jumps in position at the beginning of runs (e.g., the four runs from ~4-13 s in Fig. 1G). These jumps are not apparent in the kinesin-1 and -3 traces. What is the explanation? Is kinesin-2 binding accelerated by resisting loads more strongly than kinesin-1 and -3?

Due to the compliance of the dsDNA, the 95% limits for the initial attachment position are +/- 290 nm (Fig. S2). Thus, some apparent ‘jumps’ from the detached state are expected. We will take a closer look at why there are jumps for kinesin-2 that aren’t apparent for kinesin-1 or -3.

When comparing the durations of unloaded and stall events (Fig. 2), there is a potential for bias in the measurement, where very long unloaded runs cannot be observed due to the limited length of the microtubule (Thompson, Hoeprich, and Berger, 2013), while the duration of tethered runs is only limited by photobleaching. Was the possible censoring of the results addressed in the analysis?

Yes. Please see response to Reviewer #2 points (8) and (9) above.

The mathematical model is helpful in interpreting the data. To assess how the "slip" state contributes to the association kinetics, it would be helpful to compare the proposed model with a similar model with no slip state. Could the slips be explained by fast reattachments from the detached state?

In the model, the slip state and the detached states are conceptually similar; they only differ in the sequence (slip to detached) and the transition rates into and out of them. The simple answer is: yes, the slips could be explained by fast reattachments from the detached state. In that case, the slip state and recovery could be called a “detached state with fast reattachment kinetics”. However, the key data for defining the kinetics of the slip and detached states is the distribution of Recovery times shown in Fig. 4D-F, which required a triple exponential to account for all of the data. If we simplified the model by eliminating the slip state and incorporating fast reattachment from a single detached state, then the distribution of Recovery times would be a single-exponential with a time constant equivalent to t₁, which would be a poor fit to the experimental distributions in Fig. 4D-F.

We appreciate the efforts and helpful suggestions of all three reviewers and the Editor.

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Coppin, C.M., J.T. Finer, J.A. Spudich, and R.D. Vale. 1996. Detection of sub-8-nm movements of kinesin by high-resolution optical-trap microscopy. Proc Natl Acad Sci U S A. 93:1913-1917.

Coppin, C.M., D.W. Pierce, L. Hsu, and R.D. Vale. 1997. The load dependence of kinesin's mechanical cycle. Proc Natl Acad Sci U S A. 94:8539-8544.

Ezber, Y., V. Belyy, S. Can, and A. Yildiz. 2020. Dynein Harnesses Active Fluctuations of Microtubules for Faster Movement. Nat Phys. 16:312-316.

Hancock, W.O. 2014. Bidirectional cargo transport: moving beyond tug of war. Nat Rev Mol Cell Biol. 15:615-628.

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Kuo, Y.W., M. Mahamdeh, Y. Tuna, and J. Howard. 2022. The force required to remove tubulin from the microtubule lattice by pulling on its alpha-tubulin C-terminal tail. Nature communications. 13:3651.

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eLife Assessment

This study provides a valuable insight into how the medial and lateral entorhinal cortices interact through distinct excitatory and inhibitory pathways. Using anatomical tracing, optogenetics, and electrophysiology, the authors show that glutamatergic medial entorhinal neurons provide broad excitatory input to lateral entorhinal, while long-range SST+ interneurons deliver selective inhibition to layer I. These findings reveal a novel layer- and cell-type-specific organization of medial to lateral entorhinal connectivity with implications for spatial and episodic memory. The work is solid, but validation of injection specificity and viral spread is needed to fully confirm the anatomical interpretations; with these clarifications, this will be a significant contribution to understanding entorhinal-hippocampal circuit organization.

Reviewer #1 (Public review):

The study addresses the organisation of synaptic connections from the medial to the lateral entorhinal cortex. Classic anatomical work has suggested these connections exist, but very little is known about their identity or functional impact. The manuscript argues that these projections are mediated by glutamatergic neurons, providing excitatory input from MEC to all layers of LEC, and by SST+ve interneurons sending inhibitory projections to L1 of LEC. This appears to be the most likely interpretation of the data, although in my opinion, more could be done to rule out the possible impact of the spread of the virus/tracer from the injection site.

While this concern might seem overly picky, the importance of this level of detail is nicely shown by the authors' previous work clarifying connectivity from postrhinal to entorhinal cortices through careful analysis of similar types of data (Doan et al. 2019). If additional analyses/data can address the concern here, then I think this will be an important set of fundamental results that will influence thinking about circuit mechanisms for spatial cognition and episodic memory. In particular, it will nicely add to an emerging view that MEC and LEC can interact directly, showing that the organisation of these interactions is asymmetric and identifying a potentially interesting long-range inhibitory pathway.

Reviewer #2 (Public review):

Summary:

The manuscript by Nilssen et al. presents a comprehensive study of the circuitry linking the medial and lateral entorhinal cortices (MEC and LEC). Using a combination of anatomical tracing, optogenetics, and in vitro electrophysiology, the authors convincingly demonstrate that the MEC sends both glutamatergic and long-range inhibitory SST+ GABAergic projections to the LEC, with distinct laminar and cell-type-specific targeting. Notably, they reveal that SST+ inhibitory projections selectively suppress the activity of layer IIa neurons, whereas excitatory inputs preferentially engage neurons in layers IIb and III, thereby differentially modulating hippocampal-projecting populations.

Strengths:

The experiments are carefully executed, the results are compelling, and the conclusions are well supported by the data. This work will be of broad interest to researchers studying memory circuits, cortical inhibition, and the organization of long-range connectivity.

Weaknesses:

Although the in vivo relevance of these connections remains to be determined, this is an important and timely contribution to our understanding of entorhinal-hippocampal interactions.

Author response:

Reviewer #1:

The issue on validation of injection sites and viral spread is an important one, and we are fully aware of the risks associated with an incomplete assessment. Note that in the supplementary material, section on ‘Brain area identification’ we write the following: ‘In all neuroanatomical tracing experiments, correct placement of tracer injections into the four different areas (MEC, PER, PIR and LEC) was carefully evaluated based on known cytoarchitectonic features (see below). Electrophysiological experiments were initiated after our neuroanatomical experiments had verified the correct surgery coordinates for interrogating pathways to LEC from MEC, PIR, PER and cLEC. In patch-clamp experiments, viral injections were considered to hit the intended target area whenever the axonal innervation patterns in LEC were consistent with the patterns obtained in our neuroanatomical tracing experiments. To ensure that our injections were placed in MEC, without unintended spread to LEC, we examined the innervation patterns in DG.

In agreement with the current understanding of entorhinal innervation of DG in rodents (Steward, 1976; van Groen et al., 2003), injections targeting MEC or LEC resulted in axonal labelling in the middle one-third or outer one-third of the molecular layer of DG, respectively. Cases where the injection had clearly spread to LEC, evident from the laminar distribution of labelling in DG and labelled cell bodies in LEC, were excluded from analysis.’

In our view this provides sufficient security that we did not by mistake included intrinsic LEC projections into our dataset. In the result section, we addressed this issue as well by stating that: ‘We carefully checked all sections at and close to the levels we used for our experiments and did not observe any virally labelled neurons in LEC.’ In case of electrophysiological experiments, one normally does not secure whole brain material to exclude viral spread, but since for each animal we did record from multiple adjacent thick slices and in none did we find indications of including LEC. Finally, we included an analysis of SST projections originating from LEC (suppl Figure 1). As can be seen from panel C the local SST axonal pattern in LEC is markedly different form that seen following an injection in MEC. We aim to provide additional supplementary detail of this and include that in the text of the revised version.

Reviewer #2:

The remark that the in vivo relevance of these connections remains to be determined is absolutely correct and in the discussion we only speculated on this, since we currently do not have functional data of sufficient quality to address this. However, in an earlier version of the paper, still accessible on bioRxiv (https://biorxiv.org/cgi/content/short/2022.11.29.518323v1), we did include data on changes in expression of the immediate early gene cFos in LEC layer IIa cells upon manipulation of the SST projections from MEC within the context of conspecific memory. These data resulted in a non-significant trend, but we do not have the time, nor the financial means to extent that dataset. Therefore we cannot revise the paper in this respect.

eLife Assessment

This valuable clinical trial compares the impact of dolutegravir intensification on longitudinal measures of total HIV DNA and day 84 measures of intact HIV DNA. The trial was well-designed, and the paper is easy to read and provides hypothesis generation-level evidence that treatment intensification might decrease intact HIV DNA level in some people after 3 months. The findings are solid, with significant limitations being that study endpoints and hypotheses were not precisely defined prior to the trial, and that effect size is limited and inconsistent across trial participants.

Reviewer #1 (Public review):

Fombellida-Lopez and colleagues describe the results of an ART intensification trial in people with HIV infection (PWH) on suppressive ART to determine the effect of increasing the dose of one ART drug, dolutegravir, on viral reservoirs, immune activation, exhaustion, and circulating inflammatory markers. The authors hypothesize that ART intensification will provide clues about the degree to which low-level viral replication is occurring in circulation and in tissues despite ongoing ART, which could be identified if reservoirs decrease and/or if immune biomarkers change. The trial design is straightforward and well-described, and the intervention appears to have been well tolerated. The investigators observed an increase in dolutegravir concentrations in circulation, and to a lesser degree in tissues, in the intervention group, indicating that the intervention has functioned as expected (ART has been intensified in vivo). Several outcome measures changed during the trial period in the intervention group, leading the investigators to conclude that their results provide strong evidence of ongoing replication on standard ART. The results of this small trial are intriguing, and a few observations in particular are hypothesis-generating and potentially justify further clinical trials to explore them in depth.

Reviewer #2 (Public review):

Summary:

An intensification study with a double dose of 2nd generation integrase inhibitor with a background of nucleoside analog inhibitors of the HIV retrotranscriptase in 2, and inflammation is associated with the development of co-morbidities in 20 individuals randomized with controls, with an impact on the levels of viral reservoirs and inflammation markers. Viral reservoirs in HIV are the main impediment to an HIV cure, and inflammation is associated with co-morbidities.

Strengths:

The intervention that leads to a decrease of viral reservoirs and inflammation is quite straightforward forward as a doubling of the INSTI is used in some individuals with INSTI resistance, with good tolerability.

This is a very well documented study, both in blood and tissues, which is a great achievement due to the difficulty of body sampling in well-controlled individuals on antiretroviral therapy. The laboratory assays are performed by specialists in the field with state-of-the art quantification assays. Both the introduction and the discussion are remarkably well presented and documented.

The findings also have a potential impact on the management of chronic HIV infection.

Reviewer #3 (Public review):

The introduction does a very good job of discussing the issue around whether there is ongoing replication in people with HIV on antiretroviral therapy. Sporadic, non-sustained replication likely occurs in many PWH on ART related to adherence, drug-drug interactions and possibly penetration of antivirals into sanctuary areas of replication and as the authors point out proving it does not occur is likely not possible and proving it does occur is likely very dependent on the population studied and the design of the intervention. Whether the consequences of this replication in the absence of evolution toward resistance have clinical significance challenging question to address.

It is important to note that INSTI-based therapy may have a different impact on HIV replication events that results in differences in virus release for specific cell type (those responsible for "second phase" decay) by blocking integration in cells that have completed reverse transcription prior to ART initiation but have yet to be fully activated. In a PI or NNRTI-based regimen, those cells will release virus, whereas with an INSTI-based regimen, they will not.

Given the very small sample size, there is a substantial risk of imbalance between the groups in important baseline measures.

Comments on the revised version from the editor:

I appreciate that the authors thoroughly address the reviewer's concerns in the response letter. Most importantly, they acknowledge that "The absence of a pre-specified statistical endpoint or sample size calculation reflects the exploratory nature of the trial." This is vital because the transient impact on total HIV DNA in the intensified versus standard dose arm raises questions about any sustained or meaningful anti-reservoir effect and was also not hypothesized a priori. The authors explanation that HIV DNA may have rebounded due to clonal expansion is interesting but not assessed directly in the trial.

The greater decrease in intact HIV DNA between days 0 and 84 in the intensified arm are notable but are somewhat limited by small sample size, small effect size and lack of data between these two timepoints.

Unfortunately, the hypothesis generating nature of the conclusions which is outlined nicely in the author's response letter is only acknowledged in the discussion of the revised paper. The abstract and results are only marginally different than the original version and still read as definitive when the evidence is only hypothesis generating. For these reasons, the level of evidence remains incomplete as before.

Author response:

Reviewer #1 (Public review):

Fombellida-Lopez and colleagues describe the results of an ART intensification trial in people with HIV infection (PWH) on suppressive ART to determine the effect of increasing the dose of one ART drug, dolutegravir, on viral reservoirs, immune activation, exhaustion, and circulating inflammatory markers. The authors hypothesize that ART intensification will provide clues about the degree to which low-level viral replication is occurring in circulation and in tissues despite ongoing ART, which could be identified if reservoirs decrease and/or if immune biomarkers change. The trial design is straightforward and well-described, and the intervention appears to have been well tolerated. The investigators observed an increase in dolutegravir concentrations in circulation, and to a lesser degree in tissues, in the intervention group, indicating that the intervention has functioned as expected (ART has been intensified in vivo). Several outcome measures changed during the trial period in the intervention group, leading the investigators to conclude that their results provide strong evidence of ongoing replication on standard ART. The results of this small trial are intriguing, and a few observations in particular are hypothesis-generating and potentially justify further clinical trials to explore them in depth. However, I am concerned about over-interpretation of results that do not fully justify the authors' conclusions.

We thank Reviewer #1 for their thoughtful and constructive comments, which helped us clarify and improve the manuscript. Below, we address each of the reviewer’s points and describe the changes that we implemented in the revised version. We acknowledge the reviewer’s concern regarding potential overinterpretation of certain findings, and in the revised version we took particular care to ensure that all conclusions are supported by the data and framed within the exploratory nature of the study.

(1) Trial objectives: What was the primary objective of the trial? This is not clearly stated. The authors describe changes in some reservoir parameters and no changes in others. Which of these was the primary outcome? No a priori hypothesis / primary objective is stated, nor is there explicit justification (power calculations, prior in vivo evidence) for the small n, unblinded design, and lack of placebo control. In the abstract (line 36, "significant decreases in total HIV DNA") and conclusion (lines 244-246), the authors state that total proviral DNA decreased as a result of ART intensification. However, in Figures 2A and 2E (and in line 251), the authors indicate that total proviral DNA did not change. These statements are confusing and appear to be contradictory. Regarding the decrease in total proviral DNA, I believe the authors may mean that they observed transient decrease in total proviral DNA during the intensification period (day 28 in particular, Figure 2A), however this level increases at Day 56 and then returns to baseline at Day 84, which is the source of the negative observation. Stating that total proviral DNA decreased as a result of the intervention when it ultimately did not is misleading, unless the investigators intended the day 28 timepoint as a primary endpoint for reservoir reduction - if so, this is never stated, and it is unclear why the intervention would then be continued until day 84? If, instead, reservoir reduction at the end of the intervention was the primary endpoint (again, unstated by the authors), then it is not appropriate to state that the total proviral reservoir decreased significantly when it did not.

We agree with the reviewer that the primary objective of the study was not explicitly stated in the submitted manuscript. We clarified this in the revised manuscript (lines 361-364). As registered on ClinicalTrials.gov (NCT05351684), the primary outcome was defined as “To evaluate the impact of treatment intensification at the level of total and replication-competent reservoir (RCR) in blood and in tissues”, with a time frame of 3 months. Accordingly, our aim was to explore whether any measurable reduction in the HIV reservoir (total or replication-competent) occurred during the intensification period, including at day 28, 56, or 84. The protocol did not prespecify a single time point for this effect to occur, and the exploratory design allowed for detection of transient or sustained changes within the intensification window.

We recognize that this scope was not clearly articulated in the original text and may have led to confusion in interpreting the transient drop in total HIV DNA observed at day 28. While total DNA ultimately returned to baseline by the end of intensification, the presence of a transient reduction during this 3-month window still fits within the framework of the study’s registered objective. Moreover, although the change in total HIV DNA was transient, it aligns with the consistent direction of changes observed across the multiple independent measures, including CA HIV RNA, RNA/DNA ratio and intact HIV DNA, collectively supporting a biological effect of intensification.

We would also like to stress that this is the first clinical trial ever, in which an ART intensification is performed not by adding an extra drug but by increasing the dosage of an existing drug. Therefore, we were more interested in the overall, cumulative, effect of intensification throughout the entire trial period, than in differences between groups at individual time points. We clarified in the revised manuscript that this was a proof-of-concept phase 2 study, designed to reveal biological effects of ART intensification rather than confirm efficacy in a powered comparison. The absence of a prespecified statistical endpoint or sample size calculation reflects the exploratory nature of the trial.

(2) Intervention safety and tolerability: The results section lacks a specific heading for participant safety and tolerability of the intervention. I was wondering about clinically detectable viremia in the study. Were there any viral blips? Was the increased DTG well tolerated? This drug is known to cause myositis, headache, CPK elevation, hepatotoxicity, and headache. Were any of these observed? What is the authors' interpretation of the CD4:8 ratio change (line 198)? Is this a significant safety concern for a longer duration of intensification? Was there also a change in CD4% or only in absolute counts? Was there relative CD4 depletion observed in the rectal biopsy samples between days 0 and 84? Interestingly, T cells dropped at the same timepoints that reservoirs declined... how do the authors rule out that reservoir decline reflects transient T cell decline that is non-specific (not due to additional blockade of replication)?

We improved the Methods section to clarify how safety and tolerability were assessed during the study (lines 389-396). Safety evaluations were conducted on day 28 and day 84 and included a clinical examination and routine laboratory testing (liver function tests, kidney function, and complete blood count). Medication adherence was also monitored through pill counts performed by the study nurses.

No virological blips above 50 copies/mL were observed and no adverse events were reported by participants during the 3-month intensification period. Although CPK levels were not included in the routine biological monitoring, no participant reported muscle pain or other symptoms suggestive of muscle toxicity.

The CD4:CD8 ratio decrease noted during intensification was not associated with significant changes in absolute CD4 or CD8 counts, as shown in Figure 5. We interpret this ratio change as a transient redistribution rather than an immunological risk, therefore we do not consider it to represent a safety concern.

We would like to clarify that CD4⁺ T-cell counts did not significantly decrease in any of the treatment groups, as shown in Figure 5. The apparent decline observed concerns the CD4/CD8 ratio, which transiently dropped, but not the absolute number of CD4⁺ T cells. Moreover, although the dynamics of total HIV DNA is indeed similar to that of CD4/CD8 ratio (both declined transiently and then returned to baseline by day 84), the dynamics of unspliced RNA and unspliced RNA/total DNA ratio are clearly different, as these markers demonstrated a sustained decrease that was maintained throughout the trial period, even when the CD4/CD8 ratio already returned to baseline. Also, we observed a significant decrease in intact HIV DNA at day 84 compared to day 0. These effects cannot be easily explained by a transient decline in CD4+ cells.

(3) The investigators describe a decrease in intact proviral DNA after 84 days of ART intensification in circulating cells (Figure 2D), but no changes to total proviral DNA in blood or tissue (Figures 2A and 2E; IPDA does not appear to have been done on tissue samples). It is not clear why ART intensification would result in a selective decrease in intact proviruses and not in total proviruses if the source of these reservoir cells is due to ongoing replication. These reservoir results have multiple interpretations, including (but not limited to) the investigators' contention that this provides strong evidence of ongoing replication. However, ongoing replication results in the production of both intact and mutated/defective proviruses that both contribute to reservoir size (with defective proviruses vastly outnumbering intact proviruses). The small sample size and well-described heterogeneity of the HIV reservoir (with regard to overall size and composition) raise the possibility that the study was underpowered to detect differences over the 84-day intervention period. No power calculations or prior studies were described to justify the trial size or the duration of the intervention. Readers would benefit from a more nuanced discussion of reservoir changes observed here.

We sincerely thank the reviewer for this insightful comment. We fully agree that the reservoir dynamics observed in our study might raise several possible interpretations, and that its complexity, resulting from continuous cycles of expansion and contraction, reflects the heterogeneity of the latent reservoir. 

Total HIV DNA in PBMCs showed a transient decline during intensification (notably at day 28), ultimately returning to baseline by day 84. This biphasic pattern likely reflects the combined effects of suppression of ongoing low-level replication by an increased DTG dosage, followed by the expansion of infected cell clones (mostly harbouring defective proviruses). In other words, the transient decrease in total (intact + defective) DNA at day 28 may be due to an initial decrease in newly infected cells upon ART intensification, however at the subsequent time points this effect was masked by proliferation (clonal expansion) of infected cells with defective proviruses. Recent studies suggest that intact and defective proviruses are subjected to different selection pressures by the immune system on ART (PMID: 38337034) and their decay on therapy is different (intact proviruses are cleared much more rapidly than defectives). In addition, defective proviruses can be preferentially expanded as they can reprogram the host cell proliferation machinery (https://doi.org/10.1101/2025.09.22.676989). This explains why in our study the intact proviruses decreased, but the total proviruses did not change, between days 0 and 84, in the intensification group. Interestingly, in the control group, we observed a significant increase in total DNA at day 84 compared to day 0, with no difference for the intact DNA, which is also in line with the clonal expansion of defective proviruses.

Importantly, we observed a significant decrease in intact proviral DNA between day 0 and day 84 in the intensification group (Figure 2D). This result directly addresses the study’s primary objective: assessing the impact of intensification on the replication-competent reservoir. In comparison, as the reviewer rightly points out, total HIV DNA includes over 90% defective genomes, which limits its interpretability as a biomarker of biologically relevant reservoir changes. In addition, other reservoir markers, such as cell-associated unspliced RNA and RNA/DNA ratios, also showed consistent trends supporting a biologically relevant effect of intensification. Even in the absence of sustained changes in total HIV DNA, the coherence across the different independent measures of the reservoir (intact DNA, unspliced RNA), suggests an effect indicative of ongoing replication pre-intensification.

Regarding tissue reservoirs, the lack of substantial change in total HIV DNA between days 0 and 84 is also in line with the predominance of defective sequences in these compartments. Moreover, the limited increase in rectal tissue dolutegravir levels during intensification (from 16.7% to 20% of plasma concentrations) may have limited the efficacy of the intervention in this site.

As for the IPDA on rectal biopsies, we attempted the assay using two independent DNA extraction methods (Promega Reliaprep and Qiagen Puregene), but both yielded high DNA shearing index values, and intact proviral detection was successful in only 3 of 40 samples. Given the poor DNA integrity, these results were not interpretable.

That said, we fully acknowledge the limitations of our study, especially the small sample size, and we agree with the reviewer that caution is needed when interpreting these findings. In the revised manuscript, we adopted a more measured tone in the discussion (lines 340-346), stating that these observations are exploratory and hypothesis-generating, and require confirmation in larger, more powered studies. Nonetheless, we believe that the convergence of multiple reservoir markers pointing in the same direction constitutes a meaningful biological effect that deserves further investigation.

(4) While a few statistically significant changes occurred in immune activation markers, it is not clear that these are biologically significant. Lines 175-186 and Figure 3: The change in CD4 cells + for TIGIT looks as though it declined by only 1-2%, and at day 84, the confidence interval appears to widen significantly at this timepoint, spanning an interquartile range of 4%. The only other immune activation/exhaustion marker change that reached statistical significance appears to be CD8 cells + for CD38 and HLA-DR, however, the decline appears to be a fraction of a percent, with the control group trending in the same direction. Despite marginal statistical significance, it is not clear there is any biological significance to these findings; Figure S6 supports the contention that there is no significant change in these parameters over time or between groups. With most markers showing no change and these two showing very small changes (and the latter moving in the same direction as the control group), these results do not justify the statement that intensifying DTG decreases immune activation and exhaustion (lines 38-40 in the abstract and elsewhere).

We agree with the reviewer that the observed changes in immune activation and exhaustion markers were modest. We revised the abstract and the manuscript text (including a section header) to reflect this more accurately (lines 39, 175, 185, 253). We noted that these differences, while statistically significant (e.g., in TIGIT+ CD4+ T cells and CD38+HLA-DR+ CD8+ T cells), were limited in magnitude. We explicitly acknowledged these limitations and interpreted the findings with appropriate caution.

(5) There are several limitations of the study design that deserve consideration beyond those discussed at line 327. The study was open-label and not placebo-controlled, which may have led to some medication adherence changes that confound results (authors describe one observation that may be evidence of this; lines 146-148). Randomized/blinded / cross-over design would be more robust and help determine signal from noise, given relatively small changes observed in the intervention arm.There does not seem to be a measurement of key outcome variables after treatment intensification ceased - evidence of an effect on replication through ART intensification would be enhanced by observing changes once intensification was stopped. Why was intensification maintained for 84 days? More information about the study duration would be helpful. Table 1 indicates that participants were 95% male. Sex is known to be a biological variable, particularly with regard to HIV reservoir size and chronic immune activation in PWH. Worldwide, 50% of PWH are women. Research into improving management/understanding of disease should reflect this, and equal participation should be sought in trials. Table 1 shows differing baseline reservoir sizes between the control and intervention groups. This may have important implications, particularly for outcomes where reservoir size is used as the denominator.

We expanded the limitations section to address several key aspects raised by the reviewer: the absence of blinding and placebo control, the predominantly male study population, and the lack of postintervention follow-up. While we acknowledge that open-label designs can introduce behavioural biases, including potential changes in adherence, we now explicitly state that placebo-controlled, blinded trials would provide a more robust assessment and are warranted in future research (lines 340346). 

The 84-day duration of intensification was chosen based on previous studies and provided sufficient time for observing potential changes in viral transcription and reservoir dynamics. However, we agree that including post-intervention follow-up would have strengthened the conclusions, and we highlighted this limitation and future direction in the revised manuscript (lines 340-346). 

The sex imbalance is now clearly acknowledged as a limitation in the revised manuscript, and we fully support ongoing efforts to promote equitable recruitment in HIV research. We would like to add that, in our study, rectal biopsies were coupled with anal cancer screening through HPV testing. This screening is specifically recommended for younger men who have sex with men (MSM), as outlined in the current EACS guidelines (see: https://eacs.sanfordguide.com/eacs part2/cancer/cancerscreening-methods). As a result, MSM participants had both a clinical incentive and medical interest to undergo this procedure, which likely contributed to the higher proportion of male participants in the study.

Lastly, although baseline total HIV DNA was higher in the intensified group, our statistical approach is based on a within-subject (repeated-measures) design, in which the longitudinal change of a parameter within the same participant during the study was the main outcome. In other words, we are not comparing absolute values of any marker between the groups, we are looking at changes of parameters from baseline within participants, and these are not expected to be affected by baseline imbalances.

(6) Figure 1: the increase in DTG levels is interesting - it is not uniform across participants. Several participants had lower levels of DTG at the end of the intervention. Though unlikely to be statistically significant, it would be interesting to evaluate if there is a correlation between change in DTG concentrations and virologic / reservoir / inflammatory parameters. A positive relationship between increasing DTG concentration and decreased cell-associated RNA, for example, would help support the hypothesis that ongoing replication is occurring.

We agree with the reviewer that assessing correlations between DTG concentrations and virological, immunological, or inflammatory markers would be highly informative. In fact, we initially explored this question in a preliminary way by examining whether individuals who showed a marked increase in DTG levels after intensification also demonstrated stronger changes in the viral reservoir. While this exploratory analysis did not reveal any clear associations, we would like to emphasize that correlating biological effects with DTG concentrations measured at a single timepoint may have limited interpretability. A more comprehensive understanding of the relationship between drug exposure and reservoir dynamics would ideally require multiple pharmacokinetic measurements over time, including pre-intensification baselines. This is particularly important given that DTG concentrations vary across individuals and over time, depending on adherence, metabolism, and other individual factors.

(7) Figure 2: IPDA in tissue- was this done? scRNA in blood (single copy assay) - would this be expected to correlate with usCaRNA? The most unambiguous result is the decrease in cell-associated RNA - accompanying results using single-copy assay in plasma would be helpful to bolster this result.

As mentioned in our response to point 3, we attempted IPDA on tissue samples, but technical limitations prevented reliable detection of intact proviruses. Regarding residual viremia, we did perform ultra-sensitive plasma HIV RNA quantification but due to a technical issue (an inadvertent PBMC contamination during plasma separation) that affected the reliability of the results we felt uncomfortable including these data in the manuscript.

The use of the US RNA / Total DNA ratio is not helpful/difficult to interpret since the control and intervention arms were unmatched for total DNA reservoir size at study entry.

We respectfully disagree with this comment. The US RNA/total DNA ratio is commonly used to assess the relative transcriptional activity of the viral reservoir, rather than its absolute size. While we acknowledge that the total HIV-1 DNA levels differed at baseline between the two groups, the US RNA/total DNA ratio specifically reflects the relationship between transcriptional activity and reservoir size within each individual, and is therefore not directly confounded by baseline differences in total DNA alone.

Moreover, our analyses focus on within-subject longitudinal changes from baseline, not on direct between-group comparisons of absolute marker values. As such, the observed changes in the US RNA/total DNA ratio over time are interpreted relative to each participant's baseline, mitigating concerns related to baseline imbalances between groups.

Reviewer #2 (Public review):

Summary:

An intensification study with a double dose of 2nd generation integrase inhibitor with a background of nucleoside analog inhibitors of the HIV retrotranscriptase in 2, and inflammation is associated with the development of co-morbidities in 20 individuals randomized with controls, with an impact on the levels of viral reservoirs and inflammation markers. Viral reservoirs in HIV are the main impediment to an HIV cure, and inflammation is associated with co-morbidities.

Strengths:

The intervention that leads to a decrease of viral reservoirs and inflammation is quite straightforward forward as a doubling of the INSTI is used in some individuals with INSTI resistance, with good tolerability.

This is a very well documented study, both in blood and tissues, which is a great achievement due to the difficulty of body sampling in well-controlled individuals on antiretroviral therapy. The laboratory assays are performed by specialists in the field with state-of-the art quantification assays. Both the introduction and the discussion are remarkably well presented and documented.

The findings also have a potential impact on the management of chronic HIV infection.

Weaknesses:

I do not think that the size of the study can be considered a weakness, nor the fact that it is open-label either.

We thank Reviewer #2 for their constructive and supportive comments. We appreciate their positive assessment of the study design, the translational relevance of the intervention, and the technical quality of the assays. We also take note of their perspective regarding sample size and study design, which supports our positioning of this trial as an exploratory, hypothesis-generating phase 2 study.

Reviewer #3 (Public review):

The introduction does a very good job of discussing the issue around whether there is ongoing replication in people with HIV on antiretroviral therapy. Sporadic, non-sustained replication likely occurs in many PWH on ART related to adherence, drug-drug interactions and possibly penetration of antivirals into sanctuary areas of replication and as the authors point out proving it does not occur is likely not possible and proving it does occur is likely very dependent on the population studied and the design of the intervention. Whether the consequences of this replication in the absence of evolution toward resistance have clinical significance challenging question to address.

It is important to note that INSTI-based therapy may have a different impact on HIV replication events that results in differences in virus release for specific cell type (those responsible for "second phase" decay) by blocking integration in cells that have completed reverse transcription prior to ART initiation but have yet to be fully activated. In a PI or NNRTI-based regimen, those cells will release virus, whereas with an INSTI-based regimen, they will not.

Given the very small sample size, there is a substantial risk of imbalance between the groups in important baseline measures. Unfortunately, with the small sample size, a non-significant P value is not helpful when comparing baseline measures between groups. One suggestion would be to provide the full range as opposed to the inter-quartile range (essentially only 5 or 6 values). The authors could also report the proportion of participants with baseline HIV RNA target not detected in the two groups.

We thank Reviewer #3 for their thoughtful and balanced review. We are grateful for the recognition of the strength of the Introduction, the complexity of evaluating residual replication, and the technical execution of the assays. We also appreciate the insightful suggestions for improving the clarity and transparency of our results and discussion.

We revised the manuscript to address several of the reviewer’s key concerns. We agree that the small sample size increases the risk of baseline imbalances. We acknowledged these limitations in the manuscript (lines 327-330). For transparency, we now provide both the full range and the IQR for all parameters in Table 1. However, we would like to stress that our statistical approach is based on a within-subject (repeated-measures) design, in which the longitudinal change of a parameter within the same participant during the study was the main outcome. In other words, we are not comparing absolute values of any marker between the groups, we are looking at changes of parameters from baseline within participants, and these are not expected to be affected by baseline imbalances.

A suggestion that there is a critical imbalance between groups is that the control group has significantly lower total HIV DNA in PBMC, despite the small sample size. The control group also has numerically longer time of continuous suppression, lower unspliced RNA, and lower intact proviral DNA. These differences may have biased the ability to see changes in DNA and US RNA in the control group.

We acknowledge the significant baseline difference in total HIV DNA between groups, which we have clearly reported. However, the other variables mentioned, such as duration of continuous viral suppression, unspliced RNA levels, and intact proviral DNA, did not differ significantly between groups at baseline, despite differences in the median values (that are always present). These numerical differences do not necessarily indicate a critical imbalance.

Notably, there was no significant difference in the change in US RNA/DNA between groups (Figure 2C).

The nonsignificant difference in the change in US RNA/total DNA between groups is not unexpected, given the significant between-group differences for both US RNA and total DNA changes. Since the ratio combines both markers, it is likely to show attenuated between-group differences compared to the individual components. However, while the difference did not reach statistical significance (p = 0.09), we still observed a trend towards a greater reduction in the US RNA/total DNA ratio in the intervention group.

The fact that the median relative change appears very similar in Figure 2C, yet there is a substantial difference in P values, is also a comment on the limits of the current sample size. 

Although we surely agree that in general, the limited sample size impacts statistical power, we would like to point out that in Figure 2C, while the medians may appear similar, the ranges do differ between groups. At days 56 and 84, the median fold changes from baseline are indeed close but the full interquartile range in the DTG group stays below 1, while in the control group, the interquartile range is wider and covers approximately equal distance above and below 1. This explains the difference in p values between the groups.

The text should report the median change in US RNA and US RNA/DNA when describing Figures 2A-2C.

These data are already reported in the Results section (lines 164–166): "By day 84, US RNA and US RNA/total DNA ratio had decreased from day 0 by medians (IQRs) of 5.1 (3.3–6.4) and 4.6 (3.1–5.3) fold, respectively (p = 0.016 for both markers)."

This statistical comparison of changes in IPDA results between groups should be reported. The presentation of the absolute values of all the comparisons in the supplemental figures is a strength of the manuscript.

In the assessment of ART intensification on immune activation and exhaustion, the fact that none of the comparisons between randomized groups were significant should be noted and discussed.

We would like to point out that a statistically significant difference between the randomized groups was observed for the frequency of CD4⁺ T cells expressing TIGIT, as shown in Figure 3A and reported in the Results section (p = 0.048).

The changes in CD4:CD8 ratio and sCD14 levels appear counterintuitive to the hypothesis and are commented on in the discussion.

Overall, the discussion highlights the significant changes in the intensified group, which are suggestive. There is limited discussion of the comparisons between groups where the results are less convincing.

We observed statistically significant differences between the randomized groups for total DNA (p<0.001) and US RNA (p=0.01), as well as for the frequency of CD4⁺ T cells expressing TIGIT (p=0.048). We would like to stress that US RNA is a key marker of residual replication as it is very sensitive to de novo infection events. As discussed in the manuscript (lines 291-294), a newly infected CD4+ T lymphocyte can contain hundreds to thousands of US HIV RNA copies at the peak of infection. Therefore, a change in the US RNA level upon ART intensification is a very sensitive indicator of new infections. The fact that for US RNA we observed both a significant reduction in the intensified group and a significant difference between the groups is a strong indicator that some new infections had been occurring prior to intensification.

The limitations of the study should be more clearly discussed. The small sample size raises the possibility of imbalance at baseline. The supplemental figures (S3-S5) are helpful in showing the differences between groups at baseline, and the variability of measurements is more apparent. The lack of blinding is also a weakness, though the PK assessments do help (note 3TC levels rise substantially in both groups for most of the time on study (Figure S2).

The many assays and comparisons are listed as a strength. The many comparisons raise the possibility of finding significance by chance. In addition, if there is an imbalance at baseline outcomes, measuring related parameters will move in the same direction.

We agree that the multiple comparisons raise the possibility of chance findings but would like to stress that in an exploratory study like this it is very important to avoid a type II error. In addition, the consistent directionality of the most relevant outcomes (US RNA and intact DNA) lends biological plausibility to the observed effects.

The limited impact on activation and inflammation should be addressed in the discussion, as they are highlighted as a potentially important consequence of intermittent, not sustained replication in the introduction.

The study is provocative and well executed, with the limitations listed above. Pharmacokinetic analyses help mitigate the lack of blinding. The major impact of this work is if it leads to a much larger randomized, controlled, blinded study of a longer duration, as the authors point out.

Finally, we fully endorse the reviewer’s suggestion that the primary contribution of this study lies in its value as a proof-of-concept and foundation for future randomized, blinded trials of greater scale and duration. We highlighted this more clearly in the revised Discussion (lines 340-346).

Reviewer #1 (Recommendations for the authors):

(1) Lines 84-87: How would chronic immune activation/inflammation be expected to differ if viral antigen is being released from stable reservoirs rather than low-level replication?

This is a very insightful question. Although release of viral antigens from stable reservoirs could certainly also trigger immune activation/inflammation, the reservoir cells in PWH on long-term ART are constantly being negatively selected by the immune system (PMID: 38337034; PMID: 36596305) so that after a number of years on therapy, most proviruses are either transcriptionally silent or express only a low amount of viral RNA/antigen. Recent evidence suggests that these selected cells possess specific biological properties that include mechanisms that limit proviral gene expression (PMID: 36599977; PMID: 36599978). In comparison, low-level replication would result in de novo infection of unselected, activated CD4+ cells that are expected to produce much more viral antigen than preselected reservoir cells.

(2) Lines 249-253: There are multiple ways to explain this observation - alternatively, the total proviral DNA declined due to transient CD4 depletion.

As discussed above, CD4⁺ T-cell counts did not significantly decrease in any of the treatment groups, as shown in Figure 5. The apparent decline observed concerns the CD4/CD8 ratio, which transiently dropped, but not the absolute number of CD4⁺ T cells. Moreover, although the dynamics of total HIV DNA is indeed similar to that of CD4/CD8 ratio (both declined transiently and then returned to baseline by day 84), the dynamics of unspliced RNA and unspliced RNA/total DNA ratio is clearly different, as these markers demonstrated a sustained decrease that was maintained throughout the trial period. Also, we observed a significant decrease in intact HIV DNA at day 84 compared to day 0. These effects cannot be easily explained by a transient decline in CD4+ cells.

(3) Lines 301-305: This is a confusing explanation for not seeing an effect in tissue. Overall, there was no change in total proviral DNA in blood between days 0 and 84 either - yet the explanation for this observation is different (249-253). Was IPDA not performed on the tissue? Wouldn't this be the preferred test for reservoir depletion?

We thank the reviewer for bringing this point to our attention. We modified the Discussion to prevent the confusion (lines 303-305). As for the IPDA on tissue, we attempted this assay on the tissue samples using two independent DNA extraction methods (Promega Reliaprep and Qiagen Puregene), but both yielded high DNA shearing index values, and intact proviral detection was successful in only 3 of 40 samples. Given the poor DNA integrity, these results were not interpretable.

eLife Assessment

Using a transposon sequencing (TN-seq) approach, the authors identified key genetic determinants of drug tolerance in Mycobacterium abscessus. Given that M. abscessus is inherently resistant to multiple antibiotics, this valuable study makes a significant contribution by uncovering how antibiotic tolerance is linked to reactive oxygen species (ROS) in this non-tuberculous mycobacterial (NTM) species. The solid findings further strengthen the growing evidence that ROS play a central role in the mechanism of antibiotic action and tolerance in mycobacteria. However, the manuscript would benefit from improved clarity of presentation and corrections in the reference section.

Reviewer #1 (Public review):

Summary:

Persistence is a phenomenon by which genetically susceptible cells are able to survive exposure to high concentrations of antibiotics. This is especially a major problem when treating infections caused by slow growing mycobacteria such as M. tuberculosis and M. abscessus. Studies on the mechanisms adopted by the persisting bacteria to survive and evade antibiotic killing can potentially lead to faster and more effective treatment strategies.

To address this, in this study, the authors have used a transposon mutagenesis based sequencing approach to identify the genetic determinants of antibiotic persistence in M. abscessus. To enrich for persisters they employed conditions, that have been reported previously to increase persister frequency - nutrient starvation, to facilitate genetic screening for this phenotype. M.abs transposon library was grown in nutrient rich or nutrient depleted conditions and exposed to TIG/LZD for 6 days, following which Tn-seq was carried out to identify genes involved in spontaneous (nutrient rich) or starvation-induced conditions. About 60% of the persistence hits were required in both the conditions. Pathway analysis revealed enrichment for genes involved in detoxification of nitrosative, oxidative, DNA damage and proteostasis stress. The authors then decided to validate the findings by constructing deletions of 5 different targets (pafA, katG, recR, blaR, Mab_1456c) and tested the persistence phenotype of these strains. Rather surprisingly only 2 of the 5 hits (katG and pafA) exhibited a significant persistence defect when compared to wild type upon exposure to TIG/LZD and this was complemented using an integrative construct. The authors then investigated the specificity of delta-katG susceptibility against different antibiotic classes and demonstrated increased killing by rifabutin. The katG phenotype was shown to be mediated through the production of oxidative stress which was reverted when the bacterial cells were cultured under hypoxic conditions. Interestingly, when testing the role of katG in other clinical strains of Mab, the phenotype was observed only in one of the clinical strains demonstrating that there might be alternative anti-oxidative stress defense mechanisms operating in some clinical strains.

Strengths:

While the role of ROS in antibiotic mediated killing of mycobacterial cells have been studied to some extent, this paper presents some new findings with regards to genetic analysis of M. abscessus susceptibility, especially against clinically used antibiotics, which makes it useful. Also, the attempts to validate their observations in clinical isolates is appreciated.

Weaknesses:

Amongst the 5 shortlisted candidates from the screen, only 2 showed marginal phenotypes which limits the impact of the screening approach.

While the role of KatG mediated detoxification of ROS and involvement of ROS in antibiotic killing was well demonstrated, the lack of replication of this phenotype in some of the clinical isolates limits the significance of these findings.

Reviewer #2 (Public review):

Summary:

The work set out to better understand the phenomenon of antibiotic persistence in mycobacteria. Three new observations are made using the pathogenic Mycobacterium abscessus as an experimental system: phenotypic tolerance involves suppression of ROS, protein synthesis inhibitors can be lethal for this bacterium, and levofloxacin lethality is unaffected by deletion of catalase, suggesting that this quinolone does not kill via ROS.

Strengths:

The ROS experiments are supported in three ways: measurement of ROS by a fluorescent probe, deletion of catalase increases lethality of selected antibiotics, and a hypoxia model suppresses antibiotic lethality. A variety of antibiotics are examined, and transposon mutagenesis identifies several genes involved in phenotypic tolerance, including one that encodes catalase. The methods are adequate for making these statements.

Weaknesses:

The work can be improved by a more comprehensive treatment of prior work, especially comparison of E. coli work with mycobacterial studies.<br /> Moreover, the work still has some technical issues to fix regarding description of the methods, supplementary material, and reference formating.

Overall impact: Showing that ROS accumulation is suppressed during phenotypic tolerance, while expected, adds to the examples of the protective effects of low ROS levels. Moreover, the work, along with a few others, extends the idea of antibiotic involvement with ROS to mycobacteria. These are field-solidifying observations.

Comments on revisions:

The authors have moved this paper along nicely. I have a few general thoughts.

(1) It would be helpful to have more references to specific figures and panels listed in the text to make reading easier.

(2) I would suggest adding a statement about the importance of the work. From my perspective, the work shows the general nature of many statements derived from work with E. coli. This is important. The abstract says this overall, but a final sentence in the abstract would make it clear to all readers.

(3) The paper describes properties that may be peculiar to mycobacteria. If the authors agree, I would suggest some stress on the differences from E. coli. Also, I would place more stress on novel findings. This might be done in a section called Concluding Remarks. The paper by Shee 2022 AAC could be helpful in phrasing general properties.

(4) Several aspects still need work to be of publication quality. Examples are the materials table and the presentation of supplementary material. Reference formatting also needs attention.

Reviewer #3 (Public review):

Summary:

The manuscript demonstrates that starvation induces persister formation in M. abscesses. They also utilized Tn-Seq for the identification of genes involved in persistence. They identified the role of catalase-peroxidase KatG in preventing death from translation inhibitors Tigecycline and Linezolid. They further demonstrated that a combination of these translation inhibitors leads to the generation of ROS in PBS-starved cells.

Strengths:

The authors used high-throughput genomics-based methods for identification of genes playing a role in persistence.

Weaknesses:

The findings could not be validated in clinical strains.

Comments on revisions: No more comments for the authors.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Weaknesses:

Only 1 gene (katG) gave a strong and 1 (Mab_1456c) exhibited a minor defect. Two of the clones did not show any persistence phenotype (blaR and recR) and one (pafA) showed a minor phenotype,

We have now carried out more detailed validation studies on the Tn-Seq, with analysis of timedependent killing over 14 d. This more comprehensive analysis shows that 4 of 5 genes analyzed do indeed have antibiotic tolerance defects under the conditions that Tn-Seq predicted a survival defect (Revised Figure 3). In addition, we found that even before actual cell death, several mutants had delayed resumption of growth after antibiotic removal (Figure 3 Supplemental).

Fig 3 - Why is there such a huge difference in the extent of killing of the control strain in media, when exposed to TIG/LZD, when compared to Fig. 1C and Fig. 4. In Fig. 1C, M. abs grown in media decreases by >1 log by Day 3 and >4 log by Day 6, whereas in Fig. 3, the bacterial load decreases by <1 log by Day 3 and <2 log by Day 6. This needs to be clarified, if the experimental conditions were different, because if comparing to Fig. 1C data then the katG mutant strain phenotype is not very different.

We agree with the reviewer that there is variability in the timing and extent of cell death from experiment to experiment. As noted by the reviewer, in Figure 1C the largest decrement in survival is between day 1 - day 3 (also seen in Figure 6A). As they noted in Figure 4 the largest decrement is between day 3 – day 6 (also seen in Figure 3A, Figure 5F). In each experiment with katG mutants we carefully compare the mutant vs. the control strain within that experiment, which is more accurate than comparing the behavior of mutant in one experiment to a control in another experiment.

Reviewer #2 (Public review):

Weaknesses:

.First, word-choice decisions could better conform to the published literature. Alternatively, novel definitions could be included. In particular, the data support the concept of phenotypic tolerance, not persistence. 

We appreciate the reviewers comments, text modified.

Second, two of the novel observations could be explored more extensively to provide mechanistic explanations for the phenomena. 

We have added several additional experiments, these are detailed below in response to specific comments.

Reviewer #3 (Public review):

Weaknesses:

The findings could not be validated in clinical strains.

We understand the reviewer’s concern that the katG phenotype was only observed in one of the two clinical strains we studied. We feel that our findings are relevant beyond the ATCC 19977 strain for two reasons

(1) We have performed additional analyses of the two clinical isolates and indeed find significant accumulation of ROS following antibiotic exposure in both of these strains (revised Figure 6A).

(2) We do in fact see a role for katG in starvation-induced antibiotic tolerance in Mabs clinical strain-2. It is not surprising that different strains from a particular species may have some different responses to stresses – for example, there is wide strain-specific variability in susceptibility to different phages within a species based on which particular phage defense modules a given strain carries (for example PMID: 37160116). We speculate that different Mabs strains may express varying levels of other antioxidant factors and note that the genes encoding several such factors were identified by our Tn-Seq screen including the peroxidases ahpC, ahpD, and ahpE. Our analysis of the genetic interactions between katG and these other factors is ongoing. 

Comments/Suggestions

(1) In Fig1E, the authors show no difference in killing Mtb with or without adaptation in PBS. These data are contrary to the data presented in Figure 1B. These also do not align with the data of M. smegmatis and M. abscesses. Please discuss these observations in light of the Duncan model of persistence (Mol Microbiol. 2002 Feb;43(3):717-31.).’

The above referenced Duncan laboratory study found tolerance after prolonged starvation but did not actually examine tolerance at early time points. While some of the transcriptional and metabolic changes seen by Duncan and others are slow, other groups have described starvation responses in Mtb that are quite rapid. For example, the stringent response mediator ppGpp accumulates within a few hours after onset of starvation in Mtb (PMID: 30906866). We suspect that a rapid signaling response such as this underlies the phenotype we observe. Regarding the difference between Mtb and other mycobacterial species we also find it surprising that Mtb had a much more rapid starvation response. This is a clear species-specific difference that may reflect an adaptation of Mtb to the nutrient-limited physiologic niche within host macrophages.

(2) Line 151, the authors state that they have used an M. abscesses Tn mutant library of ~ 55,000 mutant strains. The manuscript will benefit from the description of the coverage of total TA sites covered by the mutants.

Text modified to add this detail. There are 91,559 TA sites in the abscessus genome. Thus, our Tn density is ~60%.

(3) Line 155: Please explain how long the cells were kept in an Antibiotic medium.

This technical detail was noted above on line 153 in the original text: “…and then exposed them to TIG/LZD for 6 days”. To clarify the overall conditions, we have also revised the text of the manuscript and added the detail of how long cells were passaged after removal of antibiotics.

(4) Line 201: data not shown. Delayed resumption of growth after removal of antibiotic would be helpful in indicating drug resilience. This data could enhance the manuscript.

Data now provided in Figure 3 Supplemental

(5) Figures 4C and 4F represent the kill curve. It will be good to show the date with CFU against the drug concentration in place of OD600. CFU rather than OD600 best reflects growth inhibition.

Figures 4C and 4F are measuring the minimum inhibitory concentration (MIC) to stop the overall growth of the bacterial population. While we agree that CFU could be analyzed, this would be measuring a different outcome – cell death and the minimum bactericidal concentration (MBC). In these experiments we sought to specifically examine the MIC so as to separate growth inhibition from cell death. For this we used the standard method employed by clinical microbiology laboratories for MIC, which is optical density of the culture (PMID: 10325306).

(6) Figure 5C. The authors shall show the effect of TIG/LZD on M. abscesses ROS production without the PBS adaptation. It is important to conclude that TIG/LZD induces ROS in cells. Authors should utilize ROS scavengers such as Thiourea, DFO, etc., to conclude ROS's contribution to bacterial killing following inhibition of transcription and translation.

New data added (revised Figure 5 and Figure 5 Supplemental)  

(7) Line 303. Remove "note".

Text revised. We thank the reviewer for identifying this typographical error.  

(8) The introduction and Discussion are very similar, and several lines are repeated.

Text revised with overlapping content removed.

Reviewer #1 (Recommendations for the authors):

It appears that the same datasets for PBS adapted cultures were plotted in A-C and D-F. Either this should be specifically mentioned in the legend or it might be better to integrate the non-adapted plots into A-C which would also allow easier comparison.

Appreciate the reviewer’s suggestion; text modified with added clarification to figure legend.

This manuscript is focused on M. abs and the antibiotics TIG/LZD, so the Mtb data or data using the antibiotics INH/RIF/EMB and serves more as a distraction and can be removed

We appreciate the reviewer’s perspective. However, we wish to include these data to show the similarities (and differences) in starvation-induced tolerance between the three organisms.

Fig 3 -As mentioned for Fig. 1, it appears that the same dataset was used for the control in all the figures A-E. This should be explicitly stated in the Figure legend.

Appreciate the reviewer’s suggestion; text modified with added clarification to figure legend.

The divergent results from the clinical strains are extremely interesting. It would be helpful to determine the oxidative stress levels (similar to the cellROX data shown in 5E), to tease out if the difference in katG role is because of lack of ROS induction in these strains or due to expression of alternate anti-oxidative stress defense mechanisms.

We have performed additional cellROX analysis as suggested by the reviewer and found that the ROS induction is indeed present across all three Mabs strains, but that katG is only required in one of the two strains (Strain #2). These data are now included in the revised Figure 6.

Reviewer #2 (Recommendations for the authors):

GENERAL COMMENTS

This is a nice piece of work that uses the pathogen Mabs as a test subject.

The work has findings that likely apply generally to antibiotics and mycobacteria: 1) phenotypic tolerance is associated with suppression of ROS, 2) lethal protein synthesis inhibitors act via accumulation of ROS, and 3) levofloxacin behaves in an unexpected way. Each is a new observation. However, I believe that each topic requires more work to be firmly established to be suitable for eLife.

Phenotypic tolerance: Association with suppression of ROS is important but expected. I would solidify the conclusion by performing several additional experiments. For example, confirm the lethal effect of ROS by reducing it with an iron chelator and a radical scavenger. There is a large literature on effects of iron uptake, levels, etc. on antibiotic lethality that could be applied to this question. In 2013 Imlay argued against the validity of fluorescent probes. Perhaps getting the same results with another probe would strengthen the conclusion.

We have carried out additional experiments with both an iron chelator and small molecule ROS scavengers to further test this idea but note that these experiments have several inherent limitations: 1) These compounds have highly pleiotropic effects. For example while N-acetyl cysteine (NAC) is an antioxidant it also increases mycobacterial respiration and was shown to paradoxically decrease antibiotic tolerance in M. tuberculosis (PMID: 28396391). 2) It has been shown by the Imlay group that small-molecule antioxidants are often ineffective in quenching ROS in bacteria (PMID: 388893820), making negative results difficult to interpret. Nonetheless, we present new experimental data showing that iron chelation does indeed improve the survival of antibiotic-treated Mabs (revised Figure 5).  However,  small molecule antioxidants such as thiourea do not restore antibiotic tolerance and actually increased bacterial cell death, suggesting that they may be affecting respiration in Mabs in a manner similar to that seen for NAC in Mtb. We also note that our genetic analysis, which identified numerous other genes encoding proteins with antioxidant function (Figure 2) is a strong additional argument in support of the importance of ROS in antibiotic-mediated lethality. 

Regarding the concern raised by Imlay about the validity of oxidation-sensitive dyes - this relates to concern bacterial autofluorescence induced by antibiotics that can confound analyses in some species. We have ruled this out in our analyses by using bacteria unstained by cellROX as controls to confirm that there is negligible autofluorescence in Mabs (<0.1%, Figure 5E, Figure 6A).

Protein synthesis inhibitors: At present, this is simply an observation. More work is needed to suggest a mechanism. For example, with E. coli the aminoglycosides are protein synthesis inhibitors that also cause membrane damage. Membrane damage is known to stimulate ROS-mediated killing. Your observation needs to be extended because chloramphenicol, another protein synthesis inhibitor, blocks ROS production. The lethality may be a property of mycobacteria: does it occur with E. coli (note that rifampicin is bacteriostatic with E. coli but lethal to Mtb)?

We agree with the reviewer that the mechanism underlying ROS accumulation following transcription or translational inhibition in Mabs is of significant interest. It is likely to be a mechanism different from E. coli, because in E. coli tetracyclines and rifamycins are both bacteriostatic, whereas in Mabs they are both bactericidal. Determining the mechanism by which translation inhibitors cause ROS accumulation in Mabs is an ongoing effort in our laboratory using proteomics and metabolomics, but is outside the scope of this manuscript.

Levofloxacin: This is also at the observational stage but is unexpected. In other studies, ROS is involved in quinolone-mediated killing of bacteria. Why is this not the case with Mabs? The observation should be solidified by showing the contrast with moxifloxacin, since this compound has been studied with mycobacteria (Shee 2022 AAC). With E. coli, quinolone structure can affect the relative contribution of ROS to killing (Malik 2007 AAC), as is also seen with Mtb (Malik 2006 AAC). What is happening in the present work with levofloxacin, an important anti-tuberculosis drug? Is there a structure explanation (compare with ofloxacin)?

While these are interesting questions, a detailed exploration of the structure-function relationships between different fluoroquinolone antibiotics and their varying activities on Mtb and Mabs is outside the scope of this manuscript.  

The writing is generally easy to follow. However, the concept of persistence should be changed to phenotypic tolerance with text changes throughout. I base this suggestion on the definitions of tolerance and persistence as stated in the consensus review (Balaban 2019 Nat Micro Rev). Experimentally, tolerance is seen as a gradual decline in survival following antibiotic addition; the decline is slower than seen with wild-type cells. The data presented in this paper fit that definition. In contrast, persistence refers to a rapid drop in survival followed by a distinct plateau (Balaban 2019 Nat Micro Rev; for example, see Wu Lewis AAC 2012 ). Moreover, to claim persistence, it would be necessary to demonstrate subpopulation status, which is not done. The Balaban review is an attempt to bring order to the field with respect to persistence and tolerance, since the two are commonly used without regard for a consistent definition.

We appreciate the reviewer’s suggestion; text modified in multiple places to clarify.

Another issue requiring clarification is the relationship between resistance and tolerance. Killing by antibiotics is a two-step process, as most clearly seen with quinolones. First a reversible bacteriostatic event occurs. Resistance blocks that bacteriostatic damage. Then a lethal metabolic response to that damage occurs. Tolerance selectively blocks the second, killing event, a distinct process that often involves the accumulation of ROS. Direct antibiotic-mediated damage is an additional mode of killing that also stems from the reversible, bacteriostatic damage created by antibiotics. The authors recognize the distinction but could make it clearer. Take a look at Zheng (JJ Collins) 2020, 2022.

Text modified to clarify this point

Many readers would also like to see a bit more background on Mabs. For example, does it grow rapidly? Are there features that make it a good model for studying mycobacteria or bacteria in general? The more general, the better.

Text modified, background added

Below I have listed specific comments that I hope are useful in bringing the work to publication and making it highly cited.

SPECIFIC COMMENTS

Line 30 unexpectedly. I would delete this word because the result is expected from the ROS work of Shee et al 2022 with mycobacteria. Moreover, Zeng et al 2022 PNAS showed that ROS participates in antimicrobial tolerance, and persistence is a form of tolerance (Balalban et al, 2019, Nat Micro Rev).

Text modified as per review suggestion

Line 39 key goal: this is probably untrue in the general sense stated, since bacteriostatic antibiotics are sufficient to clear infection (Wald-Dickler 2019 Clin Infect Dis). However, it is likely to be the goal for Mtb infections.

We agree with the reviewer that bacteriostatic antibiotics are effective in treating most types of infections and do not claim otherwise in the manuscript. However, from a clinical standpoint, eradication of the pathogen causing the infection is indeed the goal of antibiotic therapy in virtually all circumstances (with the exception of specific scenarios such as cystic fibrosis where it is recognized that the infecting organism cannot be fully eliminated). In most cases, the combination of bacteriostatic antibiotics and the host immune response is sufficient to achieve eradication. We have modified the manuscript text to reflect this nuance noted by the reviewer.

Line 62 several: you list three, but hipAB works via ppGpp, so the sentence needs fixing

Text modified  

Line 70 uncertain: this uncertainty is unreferenced. Since everything is uncertain, this vague phrase does not add to the story.

The reviewer makes an interesting philosophical argument. However, we would submit that some aspects of biology, for example the regulation of glycolysis, are understood in great detail. However, other mechanisms, such as the precise mechanisms of lethality for diverse antibiotics in different bacterial species, are far more uncertain and remain a subject of debate (for example PMID: 39910302). Text not modified.

Line 72 somewhat controversial: I would delete this, because the points in the Science papers by Lewis and Imlay have been clarified and in some cases refuted by prior and subsequent work.

Text modified

Line 72 presumed: this suggests that it is wrong and perhaps a different idea has replaced it. Another, and more likely view is that there is an additional mode of killing. I suggest rephrasing to be more in line with the literature.

Text modified for clarity. In this sentence “presume” refers to the historical concept that direct target inhibition was solely responsible for antibiotic lethality. As the reviewer notes, there is now significant literature that ROS (and perhaps other secondary effects) also contribute to bacterial killing.  

Line 73 However and the following might also: this phrasing, plus the presumed, misleads the reader from your intent. I suggest rephrasing.

See above re: line 72

Line 75 citations: these are inappropriate and should be changed to fit the statement. I suggest the initial paper by Collins (Kohanski 2007 Cell) a recent paper by Zhao (Zeng PNAS 2022), and a review Drlica Expert Rev Anti-infect Therapy 2021). The present citations are fine if you want to narrow the statement to mycobacteria, but the history is that the E. coli work came first and was then generalized to mycobacteria. A mycobacterial paper for ROS is Shee 2022 AAC.

We thank the reviewer for noticing that we inadvertently omitted several important E. coli-related references. These have been added.

Line 75 and 76: Conversely ... unresolved. Compelling arguments have been made that show major flaws in the two papers cited, and a large body of evidence has now accumulated showing the validity of the idea promoted by the Collins lab, beginning with Kohanski 2007. In addition to many papers by Collins, see Hong 2019 PNAS and Zeng 2022 PNAS). It is fine if you want to counter the arguments against the Lewis and Imlay papers (summarized in Drlica & Zhao 2021 Expert Rev Anti-infect Therapy), but making a blanket statement suggests that the authors are unfamiliar with the literature.

We agree with the reviewer that the weight of the evidence supports a role for antibiotic-induced ROS as an important mechanism for antibiotic lethality under many (though not all) conditions. We have revised the text to better reflect this nuance.

Line 78. Advantages over what?

Text modified

Line 80 exposure: to finish the logic you need to show that E. coli and S. aureus persisters fail to do this.

We thank the reviewer for their suggestion but studying these other organisms is outside the scope of this study. 

Line 82 whereas: this misdirects the reader. It would seem that a simple "and" is better

Text modified

Line 89 I think this paragraph is about the need to study Mabs, the subject of the present report. This paragraph could use a more appropriate topic sentence to guide the reader so that no guessing is involved. I suggest rephrasing this paragraph to make the case for studying more compelling.

Text modified

Line 96. I suggest citing several references after subinhibitory concentration of antibiotic.

The references are in the following sentence alongside the key observations.

Line 99. Genetic analysis: how does this phrase fit with the idea of persister cells arising stochastically?

There are two issues: 1) We would argue that persister formation is not completely stochastic, but rather a probability that can be modified both genetically and by environment (for example hipA PMID: 6348026). 2) Even if persister formation were totally stochastic, the survival of these cells may depend on specific genes – as we indeed find in our Tn-Seq analysis of Mabs.  

Line 106. In this paragraph you need to define persister. The consensus definition (Balaban 2019 Nat Micro Rev) is a subpopulation of tolerant cells. Tolerance is defined as the slowing or absence of killing while an antibiotic retains its ability to block growth. See Zeng 2022 PNAS for example with rapidly growing cells. Phenotypic tolerance is the absence of killing due to environmental perturbations, most notably nutrient starvation, dormancy, and growth to stationary phase. By extension, phenotypic persistence would be subpopulation status of a phenotypically tolerant cells. If you have a different definition, it is important to state it and emphasize that you disagree with the consensus statement.

Text modified  

Line 109 unexpectedly. I would delete this word, because the literature leads the reader to expect this result unless you make a clear case for Mabs being fundamentally different from other bacteria with respect to how antibiotics kill bacteria (this is unlikely, see Shee 2022 AAC). Indeed, lines 111-113 state extensions of E. coli work, although suppression of ROS in phenotypic tolerance and genetic persistence have not been demonstrated.

Text modified

Line 124 you might add, in parentheses and with references, that a property of persisters is crosspersistence to multiple antibiotic classes. This is also true for tolerance, both genetic and phenotypic. An addition will support your approach.

Text modified

Line 128 minimal

Text not modified. We appreciate the reviewer’s preference but both “minimal” and “minimum” are both widely accepted terms. Indeed, the Balaban et al 2019 consensus statement on definitions cited by the author above also uses “minimum” (PMID: 30980069), as do IDSA clinical guidelines (PMID: 39108079).

Line 130 is MIC somehow connected to killing or did you also measure killing? Note that blocking growth and killing cells are mechanistically distinct phenomena, although they are related. By being upstream from killing, blockage of growth will also interfere with killing.

Text modified

Line 133 PBS is undefined

Text modified

Line 134 increase in persisters ... you need to establish that these are not phenotypically tolerant cells. Do they constitute the entire population (tolerance)? Your data would be more indicative of persisters if you saw a distinct plateau with the PBS samples, as such data are often used to document persistence (retardation of killing is a property of tolerance, Balaban 2019). Fig. 1B is clearly phenotypic tolerance, as the entire population grows. Your data suggest that you are not measuring persistence as defined in the literature (Balaban 2019). Line 139 persister should be tolerance •

Text modified

Lines 142, 143, 144. 159, 163, 171, 181, 211, 226, 238, 246, 277, 279,289 persistent should be tolerant

Text modified

Line 146 fig 1E Mtb does not show the adaptation phenomenon and it is clearly tolerant, not persistent. This should be pointed out. As stated, you may be misleading the reader.

Text modified  

*Line 169. Please make it clear whether these genes are affecting antibiotic susceptibility (MIC will affect killing because blocking growth is upstream) or if you are dealing with tolerance (no change in MIC). These measurements are essential and should included as a table. By antibiotic response, do you mean that antibiotics change expression levels?

Regarding MICs, the data for MICs in control and katG mutant are presented in Figure 4C and 4F. Regarding ‘response’ we have clarified the text of this sentence.

Line 174 Interestingly should be as expected

Text not modified; tetracyclines do not induce ROS in E. coli and oxazolidinones have not been studied in this regard.

Line 183 you need to include citations. You can cite the ability of chloramphenicol to block ROS-mediated killing of E. coli. That allows you to use the word unexpected

Text modified

Line 199. All of the data in Fig. 3 shows tolerance, not persistence, requiring word changes in this paragraph.

Text modified

Line 226. The MIC experiment is important. You can add that this result solidifies the idea that blocking growth and killing cells are distinct phenomena. You can cite Shee 2022 AAC for a mycobacterial paper

Text modified

Line 241. The result with levofloxacin is unexpected, because the fluoroquinolones are widely reported to induce ROS, even with mycobacteria (see Shee 2022 AAC). You need to point this out and perhaps redo the experiment to make sure it is correct.

We appreciate the reviewer’s interest in this question. All experiments in this paper were repeated multiple times. This particular experiment was repeated 3 times and in all replicates the katG mutant was sensitized to translation inhibitors but not levofloxacin. Shee et al examined Mtb treated with moxifloxacin and found ROS generation, but did not assess whether a Mtb katG mutant had impaired survival. Thus, in addition to differences in: i) the species studied and ii) the particular fluoroquinolone used, the two sets of experiments were designed to address different questions (ROS accumulation vs protection by katG) . A cell might accumulate ROS without a katG mutant having impaired survival if genetic redundancy exists – a result we indeed see in our clinical Mabs strains under some conditions (new data included in revised Figure 6A).  

Line 269 Additional controls would bolster the conclusion: use of an antioxidant such as thiourea and an iron chelator (dipyridyl) both should reduce ROS effects.

New experiments performed, revised Figure 5.

Line 276 the word no is singular

Text modified

Line 284 this suggested ... in fact previous work suggested. This summary paragraph might go better as the first paragraph of the Discussion

Text modified to specify that this is in reference to the work in this manuscript

Lines 294-299 Most of this is redundant and should be deleted.

Text modified

Line 299 this species is vague

Text modified

Line 310 Do you want to discuss spoT?

Text not modified

Line 313 paragraph is largely redundant

Text modified

Line 314 controversial. As above, I would delete this, especially since it is not referenced and is unlikely to be true. If you believe it, you have the obligation to show why the ROS-lethality idea is untrue. If you are referring to Lewis and Imlay, there were almost a dozen supporting papers before 2013 and many after. This statement does not make the present work more important, so deletion costs you nothing.

Text modified

Line 314 direct disruption of targets. This is clearly not a general principle, because the quinolones rapidly kill while inhibition of gyrase by temperature-sensitive mutations does not (Kreuzer 1979 J.Bact; Steck 1985). Indeed, formation of drug-gyrase-DNA complexes is reversible: death is not.

Text modified

Line 318 as pointed out above, you have not brought this story up to date. The two papers mainly focused on Kohanski 2007, ignoring other available evidence.’’

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Line 326 you need to cite Shee 2022 AAC

Text modified

Line 342 the idea of mutants being protective is not novel, as several have been reported with E. coli studies. Thus, there is a general principle involved.

We agree that this suggests a potential general principle

Line 344. It depends on the inhibitor. For example, aminoglycosides are translation inhibitors and they also cause the accumulation of ROS.

We agree that ROS generation depends on the inhibitor, and indeed upon other variables including drug concentration, growth conditions, and bacterial species as well.  

Line 347. You need to point out the considerable data showing that the absence of catalase increases killing

Text modified

Line 363 look at Shee 2022 AAC and Jacobs 2021 AAC

Text modified, reference added.

Line 585 I suggest having a colleague provide critical comments on the manuscript and acknowledge that person.

Text not modified

eLife Assessment

The study presents important findings regarding the incidence and clinical impact of a mutation in a cardiac muscle protein and its association with the development of atrial fibrillation. The authors provide convincing evidence of electrophysiological disturbances in cells with this mutation and of its association with atrial fibrillation, which would be of interest to cardiologists. Evidence supporting the conclusion that this mutation causes atrial fibrillation would benefit from more rigorous electrophysiologic approaches.

Reviewer #1 (Public review):

Pavel et al. analyzed a cohort of atrial fibrillation (AF) patients from the University of Illinois at Chicago, identifying TTN truncating variants (TTNtvs) and TTN missense variants (TTNmvs). They reported a rare TTN missense variant (T32756I) associated with adverse clinical outcomes in AF patients. To investigate its functional significance, the authors modeled the TTN-T32756I variant using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). They demonstrated that mutant cells exhibit aberrant contractility, increased activity of the cardiac potassium channel KCNQ1 (Kv7.1), and dysregulated calcium homeostasis. Interestingly, these effects occurred without compromising sarcomeric integrity. The study further identified increased binding of the titin-binding protein Four-and-a-Half Lim domains 2 (FHL2) with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I iPSC-aCMs.

Comments on revised version:

This revised manuscript demonstrates significant improvement, notably through the inclusion of new data (Supplementary Figures 5 and 7) and expanded explanations in the main text. These additions strengthen the association between the TTN-T32756I missense variant and electrophysiological phenotypes relevant to atrial fibrillation (AF). The authors are commended for their thorough and thoughtful responses to reviewer feedback, their transparency in acknowledging limitations, and their efforts to provide mechanistic insight into the observed phenotype.

Nonetheless, several important limitations remain and should be more explicitly addressed when framing the conclusions and selecting the final manuscript title:

(1) While the data support a functional impact of the TTN-T32756I variant, the evidence does not yet definitively establish causality in the context of AF. Statements asserting a causal relationship should be softened and clearly framed as suggestive, pending further in vivo or patient-specific validation.

(2) The study models the TTN-T32756I variant in a single healthy iPSC line using CRISPR/Cas9 editing. Although this provides a genetically controlled system, the absence of validation in patient-derived iPSCs or replication across multiple isogenic lines limits the generalizability and reproducibility of the findings.

(3) The co-localization and co-immunoprecipitation (co-IP) data provide strong support for an interaction between FHL2 and the KCNQ1/KCNE1 complex. However, in the current form, the proposed mechanism remains plausible but not fully validated.

Reviewer #2 (Public review):

Summary:

The authors present data from a single-center cohort of African-American and Hispanic/Latinx individuals with atrial fibrillation (AF). This study provides insight into the incidences and clinical impact of missense variants in the Titin (TTN) gene in this population. In addition, the authors identified a single amino acid TTN missense variant (TTN-T32756I) that was further studied using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). These studies demonstrated that the Four-and-a-Half Lim domains 2 (FHL2), has increased binding with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I-iPSC-aCMs, enhancing the slow delayed rectifier potassium current (Iks) and is a potential mechanism for atrial fibrillation. Finally, the authors demonstrate that suppression of FHL2 could normalize the Iks current.

Strengths:

The strengths of this manuscript/study are listed below:

(1) This study includes a previously underrepresented population in the study the genetic and mechanistic basis of AF.

(2) The authors utilize current state-of-the-art methods to investigate the pathogenicity of a specific TTN missense variant identified in this underrepresented patient population.

(3) The findings of this study identify a potential therapeutic for treating atrial fibrillation.

Weaknesses:

(1) The authors do not include a non-AF group when evaluating the incidence and clinical significance of TTN missense variants in AF patients. The authors appropriately acknowledge this as a limitation in their single-center cohort.

(2) All other concerns from a previous version of this manuscript have been adequately addressed by the authors in this revision.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

Pavel et al. analyzed a cohort of atrial fibrillation (AF) patients from the University of Illinois at Chicago, identifying TTN truncating variants (TTNtvs) and TTN missense variants (TTNmvs). They reported a rare TTN missense variant (T32756I) associated with adverse clinical outcomes in AF patients. To investigate its functional significance, the authors modeled the TTN-T32756I variant using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). They demonstrated that mutant cells exhibit aberrant contractility, increased activity of the cardiac potassium channel KCNQ1 (Kv7.1), and dysregulated calcium homeostasis. Interestingly, these effects occurred without compromising sarcomeric integrity. The study further identified increased binding of the titin-binding protein Four-and-a-Half Lim domains 2 (FHL2) with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I iPSCaCMs.

Strengths:

This work has translational potential, suggesting that targeting KCNQ1 or FHL2 could represent a novel therapeutic strategy for improving cardiac function. The findings may also have broader implications for treating patients with rare, disease-causing variants in sarcomeric proteins and underscore the importance of integrating genomic analysis with experimental evidence to advance AF research and precision medicine.

Weaknesses

(1) Variant Identification: It is unclear how the TTN missense variant (T32756I) was identified using REVEL, as none of the patients' parents reportedly carried the mutation or exhibited AF symptoms. Are there other TTN variants identified in the three patients carrying TTN-T32756I? Clarification on this point is necessary.  

We thank the reviewer for their insightful comment. We have now clarified these in the method section.

Line 484-491: “The TTN-T32756I variant (REVEL Score: 0.58758, Supplementary Table 1) was prioritized due to its occurrence in multiple unrelated individuals within our clinical AF cohort, despite no reported family history of AF in affected individuals. While no parental inheritance was observed, the possibility of de novo origin cannot be excluded. Furthermore, this variant is located within a region overlapping a deletion mutation recently shown to cause AF in a zebrafish model, supporting its potential pathogenicity [37]. Notably, the affected individuals did not carry additional loss-of-function TTN variants.”

(2) Patient-Specific iPSC Lines: Since the TTN-T32756I variant was modeled using only one healthy iPSC line, it is unclear whether patient-specific iPSC-derived atrial cardiomyocytes would exhibit similar AF-related phenotypes. This limitation should be addressed.

We have now acknowledged this limitation in the revised manuscript.

Line 505-509: “Due to the patients' unavailability of peripheral blood mononuclear cells (PBMCs), we utilized a healthy iPSC line and introduced the TTN-T32756I variant using CRISPR/Cas9 genome editing. This approach ensures an isogenic background, thereby minimizing genetic variability and providing a controlled system to study the direct effects of the mutation.”

(3) Hypertension as a Confounding Factor: The three patients carrying TTN-T32756I also have hypertension. Could the hypertension associated with this variant contribute secondarily to AF? The authors should discuss or rule out this possibility.

We have now explicitly discussed this in the revised manuscript.

Line 362-367: “Hypertension is a common comorbidity in patients with AF and could contribute to disease progression. However, all three individuals carrying TTN-T32756I exhibited earlyonset AF (onset before 66 years), with one case occurring as early as 36 years. This suggests a potential two-hit mechanism, where genetic predisposition and comorbidities influence disease risk. Importantly, our iPSC model isolates the genetic effects of TTN-T32756I from other factors, supporting a direct pathogenic role.”

(4) FHL2 and KCNQ1-KCNE1 Interaction: Immunostaining data demonstrating the colocalization of FHL2 with the KCNQ1-KCNE1 (MinK) complex in TTN-T32756I iPSC-aCMs are needed to strengthen the mechanistic findings.

We thank the reviewer for this insightful suggestion. We agree that additional immunostaining data would further strengthen the evidence for FHL2 colocalization with the KCNQ1-KCNE1 complex in TTN-T32756I iPSC-aCMs. In line with this, we have expanded our analysis to include both co-immunoprecipitation and confocal microscopy.  As described in the revised manuscript (Lines 282–287), the colocalization between KCNE1 and FHL2 was increased by approximately threefold in TTN-T32756I iPSC-aCMs compared with WT, supporting an enhanced interaction between these proteins (Figure 5A, Supplementary Figure 6). We are generating additional immunostaining data to validate and extend these findings, and we will incorporate them into the revised submission to further substantiate the mechanistic link proposed.

Line 282-287: “…..if TTN-T32756I increases I_ks by modulating the interaction between KCNQ1KCNE1 and FHL2, we performed co-immunoprecipitation studies and confocal microscopy in both WT and TTN-T32756I-iPSC-aCMs. The co-localization between KCNE1 and FHL2 increased ~3 fold in TTN-T32756I-iPSC-aCMs, suggesting an increased interaction between them (Figure 5A, Supplementary Figure 7).”

(5) Functional Characterization of FHL2-KCNQ1-KCNE1 Interaction: To further validate the proposed mechanism, additional functional assays are necessary to characterize the interaction between FHL2 and the KCNQ1-KCNE1 complex in TTN-T32756I iPSC-aCMs.

We thank the reviewer for this valuable suggestion. We agree that additional functional assays would provide further validation of the proposed mechanism. However, we believe such in-depth characterization warrants a dedicated follow-up study and is beyond the scope of the current revision. In this work, our primary objective is to establish that the TTN missense variant can exert a detrimental effect and serve as a substrate for AF. 

Line 418-419: “Further study is needed to validate the proposed mechanism and determine if TTNmvs in other regions are associated with AF by a similar process.”

Reviewer #2 (Public review):

Summary:

The authors present data from a single-center cohort of African-American and Hispanic/Latinx individuals with atrial fibrillation (AF). This study provides insight into the incidences and clinical impact of missense variants in this population in the Titin (TTN) gene. In addition, the authors identified a single amino acid TTN missense variant (TTN-T32756I) that was further studied using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). These studies demonstrated that the Four-and-a-Half Lim domains 2 (FHL2) has increased binding with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I-iPSCaCMs, enhancing the slow delayed rectifier potassium current (Iks) and is a potential mechanism for atrial fibrillation. Finally, the authors demonstrate that suppression of FHL2 could normalize the Iks current.

Strengths:

The strengths of this manuscript/study are listed below:

(1) This study includes a previously underrepresented population in the study of the genetic and mechanistic basis of AF.

(2) The authors utilize current state-of-the-art methods to investigate the pathogenicity of a specific TTN missense variant identified in this underrepresented patient population.

(3) The findings of this study identify a potential therapeutic for treating atrial fibrillation.

Weaknesses:

(1) The authors do not include a non-AF group when evaluating the incidence and clinical significance of TTN missense variants in AF patients.

We appreciate the reviewer’s comment and acknowledge the limitation of not including a non-AF control group in our clinical analysis. As noted in the revised manuscript (Lines 347–353), our cohort was derived from a single-center registry of individuals with AF and therefore lacks a matched non-AF control population for direct comparison of TTN missense variant incidence. We agree that future studies incorporating larger, multiethnic validation cohorts with both AF and non-AF individuals, as well as evaluating AF-specific measures such as arrhythmia burden and treatment response, will be essential to fully elucidate the clinical significance of TTN missense variants in AF.

Line 347-353: “Our cohort is derived from a single-center multi-ethnic registry of individuals with AF and lacks a matched cohort of non-AF controls to compare the incidence of TTN missense variants.  Further study exploring these associations in mult-ethnic, larger validation cohorts that include both AF and non-AF individuals and examining AF-specific measures such as arrhythmia burden or treatment response will be necessary to fully understand the clinical importance of TTNmvs in AF.”

(2) The authors do not provide evidence that TTN-T32756I-iPSC-aCMs are arrhythmogenic, only that there is an increase in the Iks current and associated action potential changes. More specifically, the authors report that "compared to the WT, TTN-T32756I-iPSC-aCMs exhibited increased arrhythmic frequency," yet it is unclear what they are referring to by "arrhythmic frequency."

We thank the reviewer for this important point and for highlighting the need for clarification. In our study, the term “arrhythmic frequency” was intended to describe the increased spontaneous beating rate, irregular action potential patterns, and abnormal calcium handling observed in TTN-T32756I iPSC-aCMs compared with WT. These findings support the concept that the AF-associated TTN-T32756I variant promotes ion channel remodeling and perturbs excitation–contraction coupling, thereby creating a potential arrhythmogenic substrate for AF. To avoid ambiguity, we have removed the term “arrhythmic frequency” and revised the text for clarity and precision (Lines 222–223).

Lines 222-223: “Compared to the WT, TTN-T32756I-iPSC-aCMs exhibited increased frequency along with a significant reduction of the time to 50% and 90% decline of calcium transients (Figure 3G-I, Supplementary Figure 4F).”

(3) There seem to be discrepancies regarding the impact of the TTN-T32756I variant on mechanical function. Specifically, the authors report "both reduced contraction and abnormal relaxation in TTN-T32756I-iPSC-aCMs" yet, separately report "the contraction amplitude of the mutant was also increased . . . suggesting an increased contractile force by the TTN-T32756IiPSC-aCMs and TTN-T32756I-iPSC-CMs exhibited similar calcium transient amplitudes as the WT."

We thank the reviewer for highlighting this critical point and apologize for the lack of clarity. We intended to distinguish between changes in contractile force and contractile dynamics. Specifically, the increased contraction amplitude observed in TTN-T32756I iPSCaCMs reflects enhanced contractile force, whereas the reduced contraction duration and impaired relaxation reflect abnormalities in contractile kinetics. Together, these findings indicate that the TTN-T32756I variant alters both the strength and the temporal dynamics of contraction, consistent with dysfunctional mechanical performance. We have revised the text accordingly to more accurately convey these results (Lines 187–192).

Lines 187-192: “Compared to WT, the beating frequency of the TTN-T32756I-iPSC-aCMs was significantly increased (52 ± 7.8 vs. 98 ± 7.5 beats per min, P=0.001; Figure 2C) coupled with the reduction of the contraction duration (456.5 ± 61.45 vs 262.9 ± 48.16 msec, P=0.032; Figure 2D), the peak-to-peak time (1529 ± 195.5 vs 636.6 ± 135.8 msec, P=0.004; Supplementary Figure 3B),  and the relaxation (281.5 ± 42.95 vs 79.40 ± 21.14 msec, P=0.003; Supplementary Figure 3A).”

Reviewer #3 (Public review):

Summary:

The authors describe the abnormal contractile function and cellular electrophysiology in an iPSC model of atrial myocytes with a titin missense variant. They provide contractility data by sarcomere length imaging, calcium imaging, and voltage clamp of the repolarizing current iKs. While each of the findings is interesting, the paper comes across as too descriptive because there is no data merging to support a cohesive mechanistic story/statement, especially from the electrophysiological standpoint. There is not enough support for the title "A Titin Missense Variant Causes Atrial Fibrillation", since there is no strong causative evidence. There is some interesting clinical data regarding the variant of interest and its association with HF hospitalization, which may lead to future important discoveries regarding atrial fibrillation.

Strengths:

The manuscript is well written, and a wide range of experimental techniques are used to probe this atrial fibrillation model.

Weaknesses

(1) While the clinical data is interesting, it is essential to rule out heart failure with preserved EF as a confounder. HFpEF leads to AF due to increased atrial remodeling, so the fact that patients with this missense variant have increased HF hospitalizations does not necessarily directly support the variant as causative of AF. It could be that the variant is associated directly with HFpEF instead, and this needs to be addressed and corrected in the analyses.

We appreciate the reviewer’s insightful comment and agree that HFpEF-related atrial remodeling could represent a potential confounder in the association between TTN missense variants and AF. The primary aim of our clinical analysis was to assess the potential significance of TTNmv in AF, recognizing the inherent limitations of retrospective observational data in establishing causality. To complement this, our in vitro studies were specifically designed to demonstrate that TTNmv can alter the electrophysiological substrate, thereby predisposing to AF independent of clinical comorbidities.

While HFpEF is an important consideration, to our knowledge, no existing literature directly implicates TTNmv in HFpEF pathogenesis. In contrast, loss-of-function TTN variants are more commonly associated with HFrEF and dilated cardiomyopathy, and even these associations remain an area of active debate. To address potential confounding in our cohort, we adjusted for reduced ejection fraction in multivariable analyses of clinical outcomes. Additionally, we performed a sensitivity analysis excluding patients with nonischemic dilated cardiomyopathy (Supplementary Table 6). Together, these approaches mitigate the potential impact of heart failure subtypes on our findings, while our mechanistic studies strengthen the argument that TTNmv may contribute directly to AF susceptibility.

(2) All contractility and electrophysiologic data should be done with pacing at the same rate in both control and missense variant groups, to control for the effect of cycle length on APD and calcium loading. A shorter APD cannot be claimed when the firing rate of one set of cells is much faster than the other, since shorter APD is to be expected with a quicker rate. Similarly, contractility is affected by diastolic interval because of the influence of SR calcium content on the myocyte power stroke. So the cells need to be paced at the same rate in the IonOptix for any direct comparison of contractility. The authors should familiarize themselves with the concept of electrical restitution.

We thank the reviewer for this crucial technical comment. iPSC-derived cardiomyocytes (iPSC-CMs) are known to exhibit spontaneous automaticity due to the presence of pacemaker-like currents and reduced I_K1, which enables interrogation of their intrinsic electrophysiological properties and disease-relevant remodeling. In our study, we leveraged this feature to test the hypothesis that TTN missense variants alter electrophysiological properties through ion channel remodeling. That said, we fully agree with the reviewer that pacing iPSCCMs at a controlled cycle length is essential for minimizing rate-dependent effects on APD, calcium handling, and contractility, and would improve the interpretability of group comparisons. While iPSC-CMs with matched genetic backgrounds are expected to display broadly comparable electrophysiological profiles, biological and technical variability can influence spontaneous beating rates, thereby confounding direct comparisons. To address this, we have incorporated pacing protocols into our revised experimental design to ensure that APD and contractility measurements are obtained under identical cycle lengths, consistent with the concept of electrical restitution.

(3) It is interesting that the firing rate of the myocytes is faster with the missense variant. This should lead to a hypothesis and investigation of abnormal automaticity or triggered activity, which may also explain the increased contractility since all these mechanisms are related to the SR's calcium clock and calcium loading. See #2 above for suggestions on how to probe calcium handling adequately. Such an investigation into impulse initiation mechanisms would be compelling in supporting the primary statement of the paper since these are actual mechanisms thought to cause AF.

We thank the reviewer for this insightful suggestion. We agree that the faster firing rate observed in TTN-T32756I iPSC-aCMs raises the possibility of abnormal automaticity or triggered activity, both of which are highly relevant to AF pathophysiology. As these mechanisms are tightly coupled to calcium handling and the SR calcium clock, further probing of calcium cycling abnormalities would provide valuable mechanistic insights. While this level of investigation is beyond the scope of the current study, we view it as a compelling future direction that could directly link TTN missense variants to impulse initiation abnormalities contributing to AF. 

(4) The claim of shortened APD without correcting for cycle length is problematic. However, linking shortened APD in isolated cells alone to AF causation is more complicated. To have a setup for reentry, there must be a gradient of APD from short to long, and this can only be demonstrated at the tissue level, not at the cellular level, so reentry should not be invoked here. If shortened APD is demonstrated with correction of the cycle length problem, restitution curves can be made showing APD shortening at different cycle lengths. If restitution is abnormal (i.e. the APD does not shorten normally in relation to the diastolic interval), this may lead to triggered activity which is an arrhythmogenic mechanism. This would also tie in well with the finding of abnormally elevated iKs current since iKs is a repolarizing current directly responsible for restitution.

We thank the reviewer for this necessary clarification. We agree that isolated cell studies cannot directly demonstrate reentrant circuits and that reentry should not be inferred solely from cellular APD data. Our observation of shortened APD and abnormal beating patterns in TTN-T32756I iPSC-aCMs suggests ion channel remodeling that may predispose to arrhythmogenic conditions. Still, we recognize that tissue-level gradients of APD are required to establish reentry as a mechanism. Accordingly, we have removed mention of “the reentrant mechanism” from the revised manuscript and limited our interpretation to the cellular findings. Future studies incorporating pacing protocols and restitution curve analyses will be valuable in determining whether abnormal APD restitution and elevated I_Ks contribute to triggered activity, thereby providing a more direct mechanistic link to AF (Lines 101–105).

Lines 101-105: “Our study showed that the TTN-T32756I iPSC-aCMs exhibited a striking AF-like EP phenotype in vitro, and transcriptomic analyses revealed that the TTNmv increases the activity of the FHL2, which then modulates the slow delayed rectifier potassium current (I_Ks) to cause AF.” 

Reviewer #1 (Recommendations for the authors):

Electrophysiological Phenotype in Ventricular CMs: Has the iPSC line carrying TTN-T32756I been differentiated into ventricular cardiomyocytes (iPSC-vCMs)? The reported cellular phenotype in iPSC-aCMs does not seem to specifically reflect an AF phenotype. Does the variant produce similar electrophysiological alterations in iPSC-vCMs?

We thank the reviewer for this thoughtful comment. To date, we have not differentiated the TTN-T32756I iPSC line into ventricular cardiomyocytes (iPSC-vCMs). Our current work focuses on iPSC-aCMs, where we demonstrate that the AF-associated TTNT32756I variant induces ion channel remodeling and abnormal beating patterns, thereby creating a potential arrhythmogenic substrate relevant to AF. We agree that investigating whether this variant produces similar or distinct electrophysiological alterations in iPSC-vCMs would provide essential insights into chamber-specific effects and broaden our mechanistic understanding. We have acknowledged this as a future direction in the revised manuscript (Lines 422–425).

Lines 422-425: “While we have not yet explored the effect of TTN-T32756I in iPSC-derived ventricular cardiomyocytes, it would be interesting to investigate whether this variant produces similar or distinct electrophysiological alterations in the ventricular cardiomyocytes.”

eLife Assessment

This study provides valuable insights into the role of the NF-kB and IKK signaling pathways in γδ T cell development and survival, using robust genetic mouse models. While the research is methodologically sound, some conclusions require further evidence, with incomplete analyses, particularly regarding cell-intrinsic effects and mechanistic details. Overall, the findings are significant for immunologists interested in innate-like T cell biology and advancing the understanding of γδ T cell differentiation and maintenance.

Reviewer #1 (Public review):

Summary:

The NF-kB signaling pathway plays a critical role in the development and survival of conventional alpha beta T cells. Gamma delta T cells are evolutionarily conserved T cells that occupy a unique niche in the host immune system and that develop and function in a manner distinct from conventional alpha beta T cells. Specifically, unlike the case for conventional alpha beta T cells, a large portion of gamma delta T cells acquire functionality during thymic development, after which they emigrate from the thymus and populate a variety of mucosal tissues. Exactly how gamma delta T cells are functionally programmed remains unclear. In this manuscript, Islam et al. use a wide variety of mouse genetic models to examine the influence of the NF-kB signaling pathway on gamma delta T cell development and survival. They find that the inhibitor of kappa B kinase complex (IKK) is critical to the development of gamma delta T1 subsets, but not adaptive/naïve gamma delta T cells. In contrast, IKK-dependent NF-kB activation is required for their long-term survival. They find that caspase 8-deficiency renders gamma delta T cells sensitive to RIPK1-mediated necroptosis, and they conclude that IKK repression of RIPK1 is required for the long-term survival of gamma delta T1 and adaptive/naïve gamma delta T cells subsets. These data will be invaluable in comparing and contrasting the signaling pathways critical for the development/survival of both alpha beta and gamma delta T cells.

The conclusions of the paper are mostly well-supported by the data, but some aspects need to be clarified.

(1) The authors appear to be excluding a significant fraction of the TCRlow gamma delta T cells from their analysis in Figure 1A. Since this population is generally enriched in CD25+ gamma delta T cells, this gating strategy could significantly impact their analysis due to the exclusion of progenitor gamma delta T cell populations.

(2) The overall phenotype of the IKKDeltaTCd2 mice is not described in any great detail. For example, it is not clear if these mice possess altered thymocyte or peripheral T cell populations beyond that of gamma delta T cells. Given that gamma delta T cell development has been demonstrated to be influenced by gamma delta T cells (i.e, trans-conditioning), this information could have aided in the interpretation of the data. Related to this, it would have been helpful if the authors provided a comparison of the frequencies of each of the relevant subsets, in addition to the numbers.

(3) The manner in which the peripheral gamma delta T cell compartment was analyzed is somewhat unclear. The authors appear to have assessed both spleen and lymph node separately. The authors show representative data from only one of these organs (usually the lymph node) and show one analysis of peripheral gamma delta T cell numbers, where they appear to have summed up the individual spleen and lymph node gamma delta T cell counts. Since gamma deltaT17 and gamma deltaT1 are distributed somewhat differently in these compartments (lymph node is enriched in gamma deltaT17, while spleen is enriched in gamma deltaT1), combining these data does not seem warranted. The authors should have provided representative plots for both organs and calculated and analyzed the gamma delta T cell numbers for both organs separately in each of these analyses.

(4) The authors make extensive use of surrogate markers in their analysis. While the markers that they choose are widely used, there is a possibility that the expression of some of these markers may be altered in some of their genetic mutants. This could skew their analysis and conclusions. A better approach would have been to employ either nuclear stains (Tbx21, RORgammaT) or intracellular cytokine staining to definitively identify functional gamma deltaT1 or gamma deltaT17 subsets.

(5) The analysis and conclusion of the data in Figure 3A is not convincing. Because the data are graphed on log scale, the magnitude of the rescue by kinase dead RIPK1 appears somewhat overstated. A rough calculation suggests that in type 1 game delta T cells, there is ~ 99% decrease in gamma delta T cells in the Cre+WT strain and a ~90% decrease in the Cre+KD+ strain. Similarly, it looks as if the numbers for adaptive gamma delta T cells are a 95% decrease and an 85% decrease, respectively. Comparing these data to the data in Figure 5, which clearly show that kinase dead RIPK1 can completely rescue the Caspase 8 phenotype, the conclusion that gamma delta T cells require IKK activity to repress RIPK1-dependent pathways does not appear to be well-supported. In fact, the data seem more in line with a conclusion that IKK has a significant impact on gamma delta T cell survival in the periphery that cannot be fully explained by invoking Caspase8-dependent apoptosis or necroptosis. Indeed, while the authors seem to ultimately come to this latter conclusion in the Discussion, they clearly state in the Abstract that "IKK repression of RIPK1 is required for survival of peripheral but not thymic gamma delta T cells." Clarification of these conclusions and seeming inconsistencies would greatly strengthen the manuscript. With respect to the actual analysis in Figure 3A, it appears that the authors used a succession of non-parametric t-tests here without any correction. It may be helpful to determine if another analysis, such as ANOVA, may be more appropriate.

(6) The conclusion that the alternative pathway is redundant for the development and persistence of the major gamma delta T cell subsets is at odds with a previous report demonstrating that Relb is required for gamma delta T17 development (Powolny-Budnicka, I., et al., Immunity 34: 364-374, 2011). This paper also reported the involvement of RelA in gamma delta T17 development. The present manuscript would be greatly improved by the inclusion of a discussion of these results.

(7) The data in Figures 1C and 3A are somewhat confusing in that while both are from the lymph nodes of IKKdeltaTCD2 mice, the data appear to be quite different (In Figure 3A, the frequency of gamma delta T cells increases and there is a near complete loss of the CD27+ subset. In Figure 1A, the frequency of gamma delta T cells is drastically decreased, and there is only a slight loss of the CD27+ subset.)

Reviewer #2 (Public review):

This study presents a comprehensive genetic dissection of the role of IKK signaling in the development and maintenance of lymphoid gd T cells. By employing a variety of conditional and mutant mouse models, the authors demonstrate that IKK-dependent NF-κB activation is essential for the generation of type 1 gd T cells, while adaptive gd T cells require this pathway primarily for long-term survival. The use of multiple complementary genetic strategies, including IKK deletion and modulation of RIPK1 and CASPASE8 activity, provides robust mechanistic insight into subset-specific regulation of gd T cell homeostasis. Overall, the study provides mechanistic insight for IKK-dependent regulation of gd T cell development and peripheral maintenance. However, additional experiments can be performed to improve this manuscript and its interpretations.

Specific Concerns:

(1) All approaches used confer changes to the entire T cell compartment. Therefore, the authors are unable to resolve whether the observations are mediated by direct and/or indirect effects (e.g., disorganized lymphoid architecture impacting maintenance/survival/homing).

(2) Assessment of factors that impact T cell numbers in the periphery is necessary. Are there observable changes to the proliferation, survival, and migration of gd T cell subsets?

(3) TCRd chain usage, especially among type 3 gd T cells, should be assessed.

(4) The functional consequences of IKK signaling on gd T cells were largely unaddressed. Cytokine analyses were performed only in the RIPK1D138N Casp8∆TCD2 model, leaving open the question of how canonical NF-κB-dependent signaling impacts the long-term functionality of gd T cells.

(5) The authors suggest that Caspase 8 is required for the development and maintenance of type 3 gd T cells. While the authors discussed the limitations of assessing adult mice in interpreting the data, it seems like a relatively straightforward experiment to perform.

(6) While analyses of Casp8∆TCD2 RIPK1D138N mice suggest that loss of adaptive and type 1 gamma delta T cells in Casp8∆TCD2 animals is due to necroptosis, the contribution of RIPK3 kinase activity remains unexamined. RIPK3 activity determines whether cells die via necroptosis or apoptosis in RIPK1/Caspase8-dependent signaling, and inclusion of this analysis would strengthen mechanistic insights.

(7) Canonical NF-κB signaling through cRel alone was not evaluated, leaving a gap in the understanding of transcriptional pathways required for gd T cell subsets.

Reviewer #3 (Public review):

Summary

The regulation of NF-κB signaling is complex and central to the differentiation and homeostasis of αβT cells, essential to adaptive immunity. γδ T cells are a distinct population that responds to stress/injury-induced cues by producing inflammatory cytokines, representing an important bridge between innate and adaptive immunity. This study from Islam et al. demonstrates that the IKK complex, a central regulator of NF-κB signaling, plays distinct and essential roles in the differentiation and maintenance of γδ T cells. The authors use elegant murine genetic models to generate clear data that disentangle these requirements in vivo.

Although NF-κB activity was found to be dispensable for specification of γδ T cell progenitors and the generation of adaptive γδ T cells, it was required for both the ontogeny of type 1 γδ T cells and the survival of mature adaptive γδ T cells. Subunit-specific analyses revealed parallels with αβ T cells: RELA was necessary for type 1 γδ T cell development, while maintenance of adaptive γδ T cells relied upon redundancy between REL subunits, with cREL and p50 compensating in the absence of RELA but not vice versa. These findings reflect distinct biological requirements for ontogeny versus maintenance, likely driven by differences in receptor signaling, such as TCR and TNFRSF family members. Moreover, IKK also maintained γδ T cell survival through repression of RIPK1-mediated cell death, echoing its dual role in αβ T cells, where it both prevents TNF-induced apoptosis and provides NF-κB-dependent survival signals.

Strengths:

The multiple, unique murine genetic models employed for detailed analysis of in vivo γδ T cell differentiation and homeostasis are a major strength of this paper. NF-κB signaling processes are devilishly complex. The conditional mutants generated for this study disentangle the requirements for the various IKK-regulated pathways in γδ T cell differentiation, cell survival, and homeostasis. Data are clearly presented and suitably interpreted, with a helpful synthesis provided in the Discussion. These data will provide a definitive account of the requirements for NF-κB signaling in γδ T cells and provide new genetic models for the community to further study the upstream signals.

Weaknesses:

The paper would benefit greatly from a graphical abstract that could summarize the key findings, making the key findings accessible to the general immunology or biochemistry reader. Ideally, this graphic would distinguish the requirements for NF-κB signals sustaining thymic γδ T cell differentiation from peripheral maintenance, taking into account the various subsets and signaling pathways required. In addition, the authors should consider adding further literature comparing the requirements for NF-κB /necroptosis pathways in regulating other non-conventional T cell populations, such as iNKT, MAIT, or FOXP3+ Treg cells. These data might help position the requirements described here for γδ T cells compared to other subsets, with respect to homeostatic cues and transcriptional states.

Last and least, there are multiple grammatical errors throughout the manuscript, and it would benefit from further editing. Likewise, there are some minor errors in figures (e.g., Figure 3A, add percentage for plot from IKKDT.RIPK1D138N mouse; Figure 7, "Adative").

eLife Assessment

This study is useful because it challenges the widely accepted notion that muscle stem cell numbers decline with aging, providing novel insights into population heterogeneity and the identification of new surface markers for geriatric MuSCs. However, the evidence is considered incomplete due to insufficient quantitative comparisons of absolute cell numbers, limited analysis of age groups (particularly the lack of "aged" mice as opposed to geriatric), and the need for further functional and mechanistic validation of key subpopulations. Additional concerns that require clarification include the lack of statistical rigor in some experiments, the presentation of supporting data not being complete, and the overextension of claims relating to senescence and new marker validation. Overall, while the findings advance understanding of MuSC aging, the conclusions drawn by the authors should be strengthened with expanded experiments and more rigorous data analysis.

Reviewer #1 (Public review):

It is widely accepted that the number of muscle stem cells (MuSCs) declines with aging, leading to diminished regenerative capacity. In this study, when MuSCs were labeled with YFP at a young age, the authors found that the YFP-positive MuSC population remained stable with aging. However, VCAM1 and Pax7 expression levels were reduced in the YFP-positive MuSCs. These VCAM1-negative/low cells exhibited limited proliferative potential and reduced regenerative ability upon transplantation into MuSC-depleted mice. Furthermore, Vcam1-/low MuSCs were highly sensitive to senolysis and represented the population in which Vcam1 expression could be restored by DHT. Finally, the authors identified CD200 and CD63 as markers capable of detecting the entire geriatric MuSC population, including Vcam1-/low cells. Although numerous studies have reported an age-related decline in MuSC numbers, this study challenges that consensus. Therefore, the conclusions require further careful validation.

Major comments:

(1) As mentioned above, numerous studies have reported that the number of MuSCs declines with aging. The authors' claim is valid, as Pax7 and Vcam1 were widely used for these observations. However, age-related differences have also been reported even when using these markers (Porpiglia et al., Cell Stem Cell 2022; Liu et al., Cell Rep 2013). When comparing geriatric Vcam1⁺ MuSCs with young MuSCs in this study, did the authors observe any of the previously reported differences? Furthermore, would increasing the sample size in Figure 1 reveal a statistically significant difference? The lack of significance appears to result from variation within the young group. In addition, this reviewer requests the presentation of data on MuSC frequency in geriatric control mice using CD200 and CD63 in the final figure.

(2) Can the authors identify any unique characteristics of Pax7-VCAM-1 GER1-MuSCs using only the data generated in this study, without relying on public databases? For example, reduced expression of Vcam1 and Pax7. The results of such analyses should be presented.

(3) In the senolysis experiment, the authors state that GER1-MuSCs were depleted. However, no data are provided to support this conclusion. Quantitative cell count data would directly address this concern. In addition, the FACS profile corresponding to Figure 4D should be included.

(4) Figure S4: It remains unclear whether DHT enhances regenerative ability through restoration of the VCAM1 expression in GER1-MuSCs, as DHT also acts on non-MuSC populations. Analyses of the regenerative ability of Senolysis+DHT mice may help to clarify this issue.

(5) Why are there so many myonuclear transcripts detected in the single-cell RNA-seq data? Was this dataset actually generated using single-nucleus RNA-seq? This reviewer considers it inappropriate to directly compare scRNA-seq and snRNA-seq results.

Reviewer #2 (Public review):

In this study, Kim et al. explore the heterogeneity within the aged MuSC population using a mouse model that enables lineage tracing of MuSCs throughout life. The questions addressed in the manuscript are highly relevant to the fields of aging and stem cell biology, and the experimental approach overcomes limitations of earlier studies. However, some of the claims would benefit from additional data analysis, and the central claim of the identification of a "previously unrecognized subpopulation" of aged MuSCs should be evaluated in light of prior work that has also examined MuSC heterogeneity in aging.

Specific points:

(1) As a general comment that is transversal to multiple figures, several experiments should include a direct comparison to a young cohort. Previous studies have shown that the depletion of subpopulations with aging is observed early in the aging process, for example, the loss of Pax7-high MuSCs is observed already in 18‐month‐old mice (Li, 2019, doi: 10.15252/embj.2019102154). Using only mice at 12-14 months as the control group is therefore insufficient to claim that no changes occur with aging.

(2) One of the central claims of the manuscript is a challenge to the notion that MuSCs number declines with age. However, the data analysis associated with the quantification of YFP+ cells needs to be expanded to support this conclusion. The authors present YFP+ cells only as a proportion of Lin-neg cells. Since FAP numbers are known to decrease with aging, a stable proportion of YFP+ cells would simply indicate that MuSCs decline at the same rate as FAPs. To more accurately assess changes in MuSC abundance, the authors should report absolute numbers of YFP+ cells normalized to tissue mass (cells/ mg of muscle).

(3) The authors emphasize that several studies use VCAM1 as a surface marker to identify MuSCs. However, many other groups rely on α7-integrin, and according to Figure 1D, the decline in ITGA7 expression within the YFP+ population is not significant. Therefore, the suggestion that MuSC numbers have been misquantified with aging would apply only to a subset of studies. If the authors can demonstrate that YFP+ cell numbers (normalized per milligram of tissue) remain unchanged in geriatric mice, the discussion should directly address the discrepancies with studies that quantify MuSCs using the Lin−/α7-integrin+ strategy.

(4) The authors focus their attention on a population of VCAM-low/VCAM-neg subpopulation of MuSCs that is enriched in aging. However, the functional properties of this same population in middle-aged (or young) mice are not addressed. Thus, it remains unclear whether geriatric VCAM-low/VCAM-neg MuSCs lose regenerative potential or whether this subpopulation inherently possesses low regenerative capacity and simply expands during aging.

(5) According to Figure 1F, the majority of MuSCs appear to fall within the category of VCAM-low or VCAM-neg (over 80% by visual estimate). It would be important to have an exact quantification of these data. As a result, the assays testing the proliferative and regenerative capacity of VCAM-low/negative cells are effectively assessing the performance of more than 80% of geriatric MuSCs, which unsurprisingly show reduced efficiency. Perhaps more interesting is the fact that a population of VCAM-high geriatric MuSCs retains full regenerative potential. However, the existence of MuSCs that preserve regenerative potential into old age has been reported in other studies (Garcia-Prat, 2020, doi: 10.1038/s41556-020-00593-7 ; Li, 2019, doi: 10.15252/embj.2019102154). At this point, the central question is whether the authors are describing the same aging-resistant subpopulations of MuSCs using a new marker (VCAM) or whether this study truly identifies a new subpopulation of MuSCs. The authors should directly compare the YFP+VCAM+ aged cells with other subpopulations that maintain regenerative potential in aging.

(6) In Figure 3F, it is unclear from the data presentation and figure legend whether the authors are considering the average of fiber sizes in each mouse as a replicate (with three data points per condition), or applied statistical analysis directly to all individual fiber measurements. The very low p-values with n=3 are surprising. It is important to account for the fact that observations from the same mouse are correlated (shared microenvironment, mouse-specific effects) and therefore cannot be considered independent.

(7) Regarding Figure 5, it is unclear why ITGA7, a classical surface marker for MuSCs that appears unchanged in aged YFP+ MuSCs (Fig. 1F), is considered inadequate for detecting and isolating GERI-MuSCs.

Reviewer #3 (Public review):

Summary:

The manuscript by Kim et al. describes a MuSC subpopulation that loses VCam expression in geriatric muscle and shows reduced ability to contribute to muscle regeneration. They propose that this population underlies the reported decline of MuSCs in aged mice, suggesting that these cells remain present in geriatric muscle but are overlooked due to low or absent VCam expression. The identification of a subpopulation that changes with aging would be compelling and of interest to the field.

Strengths:

The authors employ a wide range of assays, from in vitro to in vivo systems, to characterize Vcam-low/negative cells from geriatric muscle. The loss of Vcam appears strong in geriatric mice. They further identify CD63 and CD200 as potential surface markers that remain stable with age, thereby enabling the isolation of MuSCs across different age groups.

Weaknesses:

Some issues remain before establishing whether this population represents a true functional subset or explains the reported decline in MuSC numbers in aged mice. A stronger fate assessment of Vcam-low/negative cells is needed to assess their propensity for cell death in vitro and in vivo (e.g., engraftment efficiency), and if this plays a role in their conclusions. Comparisons include young, middle-aged, and geriatric mice, but not aged (~24 months) mice, which are needed for direct assessment of previous reports of age-related MuSC decline. The suggestion that the Vcam-low/negative population reflects senescence appears premature, with few consistent markers for this fate, as well as the cells not exhibiting irreversible cell-cycle exit. Finally, validation of CD63 and CD200 as reliable age-independent MuSC markers requires further testing, specifically using the Pax7-YFP tracing model and co-labeling in geriatric mice.

eLife Assessment

This useful paper examined the mechanism of planar cell polarity (PCP) using Drosophila pupal wing, investigating how 'cellular level', 'molecular level' and 'tissue level' mechanisms intersect to establish PCP. This represents progress for the field and the conclusions are mostly backed up by solid data. Whereas the manuscript is sound overall, remaining concerns could be addressed by textual clarification of the concepts used in the manuscript.

[Editors' note: this paper was reviewed by Review Commons and revised by the authors.]

Reviewer #1 (Public review):

The authors use inducible Fz::mKate2-sfGFP to explore "cell-scale signaling" in PCP. They reach several conclusions. First, they conclude that cell-scale signaling does not depend on limiting pools of core components (other than Fz). Second, they conclude that cell-scale signaling does not depend on microtubule orientation, and third, they conclude that cell-scale signaling is strong relative to cell to cell coupling of polarity.

There are some interesting inferences that can be drawn from the manuscript, but there are also some significant challenges in interpreting the results and conclusions from the work as presented. I suggest that the authors 1) define "cell-scale signaling," as the precise meaning must be inferred, 2) reconsider some premises upon which some conclusions depend, 3) perform an essential assay validation, and 4) explain some other puzzling inconsistencies.

Major concerns (first round of review):

The exact meaning of cell-scale signaling is not defined, but I infer that the authors use this term to describe how what happens on one side of a cell affects another side. The remainder of my critique depends on this understanding of the intended meaning.

The authors state that any tissue wide directional information comes from pre-existing polarity and its modification by cell flow, such that the de novo signaling paradigm "bypasses" these events and should therefore not be responsive to any further global cues. It is my understanding that this is not a universally accepted model, and indeed, the authors' data seem to suggest otherwise. For example, the image in Fig 5B shows that de novo induction restores polarity orientation to a predominantly proximal to distal orientation. If no global cue is active, how is this orientation explained? The 6 hr condition, that has only partial polarity magnitude, is quite disordered. Do the patterns at 8 and 10 hrs become more proximally-distally oriented? It is stated that they all show swirls, but please provide adult wing images, and the corresponding orientation outputs from QuantifyPolarity to help validate the notion that the global cues are indeed bypassed by this paradigm.

It is implicit that, in the de novo paradigm, polarization is initiated immediately or shortly after heat shock induction. However, the results should be differently interpreted if the level of available Fz protein does not rise rapidly and then stabilize before the 6 hr time point, and instead continues to rise throughout the experiment. Western blots of the Fz::mKate2-sfGFP at time points after induction should be performed to demonstrate steady state prior to measurements. Otherwise, polarity magnitude could simply reflect the total available pool of Fz at different times after induction. Interpreting stability is complex, and could depend on the same issue, as well as the amount of recycling that may occur. Prior work from this lab using FRAP suggested that turnover occurs, and could result from recycling as well as replenishment from newly synthesized protein.

From the Fig 3 results, the authors claim that limiting pools of core proteins do not explain cell-scale signaling, a result expected based on the lack of phenotypes in heterozygotes, but of course they do not test the possibility that Fz is limiting. They do note that some other contributing protein could be.

In Fig 3, it is unclear why the authors chose to test dsh1/+ rather than dsh[null]/+. In any case, the statistically significant effect of Dsh dose reduction is puzzling, and might indicate that the other interpretation is correct. Ideally, a range including larger and smaller reductions would be tested. As is, I don't think limiting Dsh is ruled out.

The data in Fig 5 are somewhat internally inconsistent, and inconsistent with the authors' interpretation. In both repolarization conditions, the authors claim that repolarization extends only to row 1, and row 1 is statistically different from non-repolarized row 1, but so too is row 3. Row 2 is not. This makes no sense, and suggests either that the statistical tests are inappropriate and/or the data is too sparse to be meaningful. For the related boundary intensity data in Fig 6, the authors need to describe exactly how boundaries were chosen or excluded from the analysis. Ideally, all boundaries would be classified as either meido-lateral (meaning anterior-posterior) or proximal-distal depending on angle.

If the authors believe their Fig 5 and 6 analyses, how do they explain that hairs are reoriented well beyond where the core proteins are not? This would be a dramatic finding, because as far as I know, when core proteins are polarized, prehair orientation always follows the core protein distribution. Surprisingly, the authors do not so much as comment about this. The authors should age their wings just a bit more to see whether the prehair pattern looks more like the adult hair pattern or like that predicted by their protein orientation results.

Reviewer #2 (Public Review):

This paper aims to dissect the relative importance of the various cues that establish PCP in the wing disc of Drosophila, which remains a prominent and relevant model for PCP. The authors suggest that one must consider cues at three scales (molecular, cell and tissue) and specifically design tests for the importance of cell-level cues, which they call non-local cell scale signalling. They develop clever experimental approaches that allow them to track complex stability and also to induce polarity at experimentally defined times. In a first set of experiments, they restore PCP after the global cues have disappeared (de novo polarisation) and conclude from the results that another (cell scale) cue must exist. In another set of experiments, they show that de novo repolarization is robust to the dosage of various components of core PCP, leading them to conclude that there must be an underlying cell scale polarity, which, apparently, has nothing to do with microtubule or cell shape polarity. They then describe nice evidence that de novo polarisation is relatively short range both in a polarised and unpolarised field. They conclude that there is a strong cell-intrinsic polarity that remains to be characterised.

Major concerns (first round of review):

(1) The first set of repolarisation experiments is performed after the global cell rearrangements that have been shown to act as global signals. However, this approach does not exclude the possible contribution of an unknown diffusible global signal.

(2) The putative non-local cell scale signal must be more precisely defined (maybe also given a better name). It is not clear to me that one can separate cell-scale from molecular-scale signal. Local signals can redistribute within a cell (or membrane) so local signals are also cell-scale. Without a clear definition, it is difficult to interpret the results of the gene dosage experiments. The link between gene dosage and cell-scale signal is not rigorously stated. Related to this, the concluding statement of the introduction is too cryptic.

Critique:

The experiments described in this paper are of high quality with a sophisticated level of design and analysis. However, there needs to be some recalibration of the extent of the conclusions that can be drawn. Moreover, a limitation of this paper is that, despite the quality of their data, they cannot give a molecular hint about the nature of their proposed cell-scale signal.

Reviewer #3 (Public Review):

The manuscript by Carayon and Strutt addresses the role of cell-scale signaling during the establishment of planar cell polarity (PCP) in the Drosophila pupal wing. The authors induce locally the expression of a tagged core PCP protein, Frizzled, and observe and analyze the de novo establishment of planar cell polarity. Using this system, the authors show that PCP can be established within several hours, that PCP is robust towards variation in core PCP protein levels, that PCP proteins do not orient microtubules, and that PCP is robust towards 'extrinsic' re-polarization. The authors conclude that the polarization at the cell-scale is strongly intrinsic and only weakly affected by the polarity of neighboring cells.

Major comments (first round of review):

The data are clearly presented and the manuscript is well written. The conclusions are well supported by the data. 

(1) The authors use a system to de novo establish PCP, which has the advantage of excluding global cues orienting PCP and thus to focus on the cell-intrinsic mechanisms. At the same time, the system has the limitation that it is unclear to what extent de novo PCP establishment reflects 'normal' cell scale PCP establishment, in particular because the Gal4/UAS expression system that is used to induce Fz expression will likely result in much higher Fz levels compared with the endogenous levels. The authors should briefly discuss this limitation.

(2) Fig. 3. The authors use heterozygous mutant backgrounds to test the robustness of de novo PCP establishment towards (partial) depletion in core PCP proteins. The authors conclude that de novo polarization is 'extremely robust to variation in protein level'. Since the authors (presumably) lowered protein levels by 50%, this conclusion appears to be somewhat overstated. The authors should tune down their conclusion.

Significance: 

The manuscript contributes to our understanding of how planar cell polarity is established. It extends previous work by the authors (Strutt and Strutt, 2002,2007) that already showed that induction of core PCP pathway activity by itself is sufficient to induce de novo PCP. This manuscript further explores the underlying mechanisms. The authors test whether de novo PCP establishment depends on an 'inhibitory signal', as previously postulated (Meinhardt, 2007), but do not find evidence. They also test whether core PCP proteins help to orient microtubules (which could enhance cell intrinsic polarization of core PCP proteins), but, again, do not find evidence, corroborating previous work (Harumoto et al, 2010). The most significant finding of this manuscript, perhaps, is the observation that local de novo PCP establishment does not propagate far through the tissue. A limitation of the study is that the mechanisms establishing intrinsic cell scale polarity remain unknown. The work will likely be of interest to specialists in the field of PCP.

Summary of comments from the Reviewing Editor on the revised version:

In the introduction, when you refer to Figure 1, the definition of Molecular, cellular, tissue scale is indeed not too clear to outside readers. For example, when you first refer to 'cell scale' you define it 'non-local', but probably it is not clear to many readers 'non-local' means 'the mechanism that cannot be explained by 'molecular scale'. (because 'molecular scale = local' is only inferred).

The 'conclusion paragraph' at the end of the Introduction does not have conclusion (only explained 'which question was tested by which method').

Minor comments that can easily be addressed by textual edits:

– they do not explain why gene dosage affects constitutive but not de novo polarization. It seems to me that one would expect de novo to be at least as sensitive if not more.

– Unconventional nomenclature for tissue axes - mediolateral, horizontal - are frequently used. These are sometimes difficult to parse. Please stick with universally accepted anterior, posterior, proximal and distal.

Author response:

(1) General Statements

Our manuscript studies mechanisms of planar polarity establishment in vivo in the Drosophila pupal wing. Specifically we seek to understand mechanisms of ‘cell-scale signalling’ that is responsible for segregating core pathway planar polarity proteins to opposite cell edges. This is an understudied question, in part because it is difficult to address experimentally.

We use conditional and restrictive expression tools to spatiotemporally manipulate core protein activity, combined with quantitative measurement of core protein distribution, polarity and stability. Our results provide evidence for a robust cell-scale signal, while arguing against mechanisms that depend on depletion of a limited pool of a core protein or polarised transport of core proteins on microtubules. Furthermore, we show that polarity propagation across a tissue is hard, highlighting the strong intrinsic capacity of individual cells to establish and maintain planar polarity.

The original manuscript received three fair and thorough peer-reviews, which raised many important points. In response, we decided to embark on a full revision that attempts to answer all of the points. We have included new data to support our conclusions in Supplemental Figures 1, 2 and 5.

Additionally in response to the reviewers we have revised the manuscript title, which is now ‘Characterisation of cell-scale signalling by the core planar polarity pathway during Drosophila wing development’.

(2) Point-by-point description of the revisions

We thank all of the reviewers for their thorough and thoughtful review of our manuscript. They raise many helpful points which have been extremely useful in assisting us to revise the manuscript.

In response we have carried out a major revision of the manuscript, making numerous changes and additions to the text and also adding new experimental data. Specific changes are listed after our detailed response to each comment.

Reviewer #1:

[…] Major points:

The exact meaning of cell-scale signaling is not defined, but I infer that the authors use this term to describe how what happens on one side of a cell affects another side. The remainder of my critique depends on this understanding of the intended meaning.

As the reviewer points out, it is important that the meaning of the term ‘cell-scale signalling’ is clear to the reader and in response to their comment we have had another go at defining it explicitly in the Introduction to the manuscript.

Specifically, we use the term ‘cell-scale signalling’ to describe possible intracellular mechanisms acting on core protein segregation to opposite cell membranes during core pathway dependent planar polarisation. For example, this could be a signal from distal complexes at one side of the cell leading to segregation of proximal complexes to the opposite cell edge, or vice versa. See also our response to Reviewer #2 regarding the distinction between ‘molecular-scale’ and ‘cell-scale’ signalling. 

Changes to manuscript: Revised definition of ‘cell-scale signalling’ in Introduction.

The authors state that any tissue wide directional information comes from pre-existing polarity and its modification by cell flow, such that the de novo signaling paradigm "bypasses" these events and should therefore not be responsive to any further global cues. It is my understanding that this is not a universally accepted model, and indeed, the authors' data seem to suggest otherwise. For example, the image in Fig 5B shows that de novo induction restores polarity orientation to a predominantly proximal to distal orientation. If no global cue is active, how is this orientation explained?

We assume that the reviewer’s point is that it is not universally accepted that de novo induction after hinge contraction leads to uncoupling from global cues (rather than that it is not accepted that hinge contraction remodels radial polarity to a proximodistal pattern). We are (we believe) the only lab that has used de novo induction as a tool, and we’re not aware of any debate in the literature about whether this bypasses global cues. Nevertheless, we accept that it is hard to prove there is no influence of global cues, when the nature of those cues and the time at which they act remain unclear. Below we summarise the reasons why we believe there are not significance effects of global cues in our experiments that would influence the interpretation of our results.

First, our reading of the literature supports a broad consensus that an early radial core planar polarity pattern is realigned by cell flow produced by hinge contraction beginning at around 16h APF (e.g. Aigouy et al., 2010; Strutt and Strutt, 2015; Aw and Devenport, 2017; Butler and Wallingford, 2017; Tan and Strutt, 2025). Taken at face value, this suggests that there are ‘radial’ cues present prior to hinge contraction, maybe coming from the wing margin – arguably these radial cues could be Ft-Ds or Wnts or both, given they are expressed in patterns consistent with such a role (notwithstanding the published evidence arguing against roles for either of these cues). It then appears that hinge contraction supercedes these cues to convert a radial pattern to a proximodistal pattern – whether the radial cues that affect the core pathway earlier remain active after hinge contraction is unclear, although both Ft-Ds and Wnts appear to maintain their ‘radial’ patterns beyond the beginning of hinge contraction (e.g. Merkel et al., 2014; Ewen-Campen et al., 2020; Yu et al., 2020).

We think that the reviewer is proposing the presence of a proximodistal cue that is active in the proximal region of the wing that we use for our experiments shown e.g. in Fig.5, and that this cue orients core polarity here (but not elsewhere in the wing) in a time window after 18h APF. Ft-Ds and Wnts do not seem to be plausible candidates as they are still in ‘radial’ patterns. This leaves either an unknown proximodistal cue (a gradient of some unknown signalling molecule?), or possibly some ability of hinge contraction to align proximodistal polarity specifically in this wing region but not elsewhere. We cannot definitively rule out either of these possibilities, but neither do we think there is sufficient evidence to justify invoking their existence to explain our observations.

In particular, the reason that we don’t think there is a proximodistal cue in the proximal part of the wing after 18h APF, is that work from our lab shows that induction of Fz or Stbm expression at times around or after the start of hinge contraction (i.e. >16 h APF) results in increasing levels of trichome swirling with polarity not being coordinated with the tissue axis either proximally or distally (Strutt and Strutt, 2002; Strutt and Strutt 2007). Our simplest interpretation for this is that induction at these stages fails to establish the early radial pattern of core pathway polarity and hence hinge contraction cannot reorient radial to proximodistal. If hinge contraction alone could specify proximodistal polarity in the absence of the earlier radial polarity, then we would not expect to see swirling over much of the proximal wing (where the forces from hinge contraction are strongest (Etournay et al., 2015)).

In this manuscript, our earliest de novo experiments begin with Fz induction at 18h APF (de novo 10h), then at 20h APF (de novo 8h) and at 22h APF (de novo 6h). The image in Fig. 5B, referred to by the reviewer, is of a wing where Fz is induced de novo at 22 h APF. In these wings, as expected, the core proteins localise asymmetrically in stereotypical swirling patterns throughout the wing surface (see Fig. 2M and also Strutt and Strutt, 2002; Strutt and Strutt 2007), but – usefully for our experiments – they broadly localise along the proximal-distal axis in the region analysed in Fig. 5B. Given the strong swirling in surrounding regions when inducing at >20h APF, we feel reasonably confident in assuming that the pattern is not due to a proximodistal cue present in the proximal wing.

We appreciate that the original manuscript did not show images including the trichome pattern in adjacent regions, so this point would not have been clear, but we now include these in Supplementary Fig. 5. We have also added a note in the legend to Fig. 5B to clarify that the proximodistal pattern seen is local to this wing region. We apologise for this oversight and the confusion caused and appreciate the feedback.

The 6 hr condition, that has only partial polarity magnitude, is quite disordered. Do the patterns at 8 and 10 hrs become more proximally-distally oriented? It is stated that they all show swirls, but please provide adult wing images, and the corresponding orientation outputs from QuantifyPolarity to help validate the notion that the global cues are indeed bypassed by this paradigm.

In all three ‘normal’ de novo conditions (6h, 8h and 10h), regardless of the time of induction, the polarity orientation patterns of Fz-mKate2 in pupal and adult wings are very similar in the experimentally analysed region (Fig. S5B-E). The strong local hair swirling agrees with the previous published data (Strutt and Strutt, 2002; Strutt and Strutt 2007). Overall, we don’t see any evidence that the 10h de novo induction results in more proximodistally coordinated polarity than the 8h or 6h conditions. This is consistent with our contention that there is no global cue present at these stages, which presumably would have a stronger effect when core pathway activity was induced at earlier stages.

Changes to manuscript: Added additional explanation of the ‘de novo induction’ paradigm and why we believe the resulting polarity patterns are unlikely to be influenced by any global signals in Introduction and Results section ‘Induced core protein relocalisation…’. Added quantification of polarity in the experiment region proximal to the anterior cross-vein in pupal wings (Fig.S5E-E’’’) and zoomed-out images of the surrounding region in adult wings showing that the polarity pattern does not become more proximodistal when induction time is longer, and also that there is not overall proximodistal polarity in proximal regions of the wing (Fig.S5B-D), arguing against an unknown proximodistal polarity cue at these stages of development.

In the de novo paradigm, polarization is initiated immediately or shortly after heat shock induction. However, the results should be differently interpreted if the level of available Fz protein does not rise rapidly and then stabilize before the 6 hr time point, and instead continues to rise throughout the experiment. Western blots of the Fz::mKate2-sfGFP at time points after induction should be performed to demonstrate steady state prior to measurements. Otherwise, polarity magnitude could simply reflect the total available pool of Fz at different times after induction. Interpreting stability is complex, and could depend on the same issue, as well as the amount of recycling that may occur. Prior work from this lab using FRAP suggested that turnover occurs, and could result from recycling as well as replenishment from newly synthesized protein. 

The reviewer raises an important point, which we agree could confound our experimental interpretations. As suggested we have now carried out western blotting and quantitation for Fz::mKate2-sfGFP levels and added these data to Fig.S1 (Fig. S1C,D). Quantified Fz is not significantly different between the three de novo polarity induction timings and not significantly different compared to constitutive Fz::mKate2-sfGFP expression (although there is a trend towards increasing Fz::mKate2-sfGFP protein levels with increasing induction times). These data are consistent with Fz::mKate2-sfGFP being at steady state in our experiments and that levels are sufficient to achieve normal polarity (as constitutive Fz::mKate2-sfGFP does so). Therefore it is unlikely that differing protein levels explain the differing polarity magnitudes at the different induction times. Interestingly, Fz::mKate2-sfGFP levels are lower than endogenous Fz levels, possibly due to lower expression or increased turnover/reduced recycling.

Changes to manuscript: Added western blot analysis of Fz::mKate2-sfGFP expression under 10h, 8h and 6h induction conditions vs endogenous Fz expression and constitutive Fz::mKate2sfGFP expression (Fig.S1C-D) and discussed in Results section ‘Planar polarity establishment is…’.

From the Fig 3 results, the authors claim that limiting pools of core proteins do not explain cellscale signaling, a result expected based on the lack of phenotypes in heterozygotes, but of course they do not test the possibility that Fz is limiting. They do note that some other contributing protein could be. 

Previously published results from our lab (Strutt et al., 2016 Cell Reports; Supplemental Fig. S6E) show that in a heterozygous fz mutant background, Fz protein levels are not affected by halving the gene dosage when compared to wt, suggesting that Fz is most likely produced in excess and is not normally limiting, but that protein that cannot form complexes may be rapidly degraded. We have now added this information to the text.

Changes to manuscript: Added explanation in text that Fz levels had previously been shown to not be dosage sensitive in Results section ‘Planar polarity establishment is…’ and also added a caveat to the Discussion about not directly testing Fz.

In Fig 3, it is unclear why the authors chose to test dsh1/+ rather than dsh[null]/+. In any case, the statistically significant effect of Dsh dose reduction is puzzling, and might indicate that the other interpretation is correct. Ideally, a range including larger and smaller reductions would be tested. As is, I don't think limiting Dsh is ruled out. 

Concerning the choice of dsh allele, we appreciate the query of the reviewer regarding use of dsh[1] instead of a null, as there might be a concern that dsh[1] would give a less strong phenotype. The answer is that over more than two decades we and others have never found any evidence that dsh[1] does not act as a ‘null’ for planar polarity in the pupal wing, and furthermore use of dsh[1] preserves function in Wg signalling – and we would prefer to rule out any phenotypic effects due to any potential cross-talk between the two pathways that might be seen using a complete null. To expand on this point, dsh[1] mutant protein is never seen at cell junctions (Axelrod 2001; Shimada et al., 2001; our own work), and by every criteria we have used, planar polarity is completely disrupted in hemizygous or homozygous mutants e.g. see quantifications of polarity in (Warrington et al., 2017 Curr Biol).

In terms of the broader point, whether we can rule out Dsh being limiting, we were very careful to be clear that we did not see evidence for Dsh (or other core proteins) being limiting in terms of ‘rates of core pathway de novo polarisation’. When the reviewer says ‘the statistically significant effect of Dsh dose reduction is puzzling’ we believe they are referring to the data in Fig. 3J, showing a small but significantly different reduction in stable Fz in de novo 6h conditions (also seen in 8h de novo conditions, Fig. S3I). As Dsh is known to stabilise Fz in complexes (Strutt et al., 2011 Dev Cell; Warrington et al., 2017 Curr Biol), in itself this result is not wholly surprising. Nevertheless, while this shows that halving Dsh levels does modestly reduce Fz stability, it does not alter our conclusion that halving Dsh levels does not affect Fz polarisation rate under either 6h or 8h de novo conditions.

Unfortunately, we do not have available to us a practical way of achieving consistent intermediate reductions in Dsh levels (e.g. a series of verified transgenes expressing at different levels). Levels of all the core proteins could be dialled down using transgenes, to see when the system breaks, and indeed we have previously published that lower levels of polarity are seen if Fmi levels are <<50% or if animals are transheterozygous for pk, stbm, dgo or dsh, pk, stbm, dgo simultaneously (Strutt et al., 2016 Cell Reports). However, it seems to be a trivial result that eventually the ability to polarise is lost if insufficient core proteins are present at the junctions. For this reason we have focused on a simple set of experiments reducing gene dosage singly by 50% under two de novo induction conditions, and have been careful to state our results cautiously. The assays we carried out were a great deal of work even for just the 5 heterozygous conditions tested.

We believe that the experiments shown effectively make the point that there is no strong dosage sensitivity – and it remains our contention that if protein levels were the key to setting up cell-scale polarity, then a 50% reduction would be expected to show an effect on the rate of polarisation. We further note that as Fz::mKate2-sfGFP levels are lower than endogenous Fz levels (see above), the system might be expected to be sensitised to further dosage reductions, and despite this we failed to see an effect on rate of polarisation.

We note that Reviewer #3 made a similar point about whether we can rule out dosage sensitivity on the basis of 50% reductions in protein level. To address the comments of both reviewers we had now added some further narrative and caveats in the text.

In a similar vein, Reviewer #2 requested data on whether dosage reduction altered protein levels by the expected amount. We have now added further explanation/references and western blot data to address this.

Changes to manuscript: Added more explanation of our choice of dsh[1] as an appropriate mutant allele to use in Results section ‘Planar polarity establishment is…’. Added some narrative and caveats regarding whether lowering levels more than 50% would add to our findings in the Discussion. Revised conclusions to be more cautious including altering section title to read ‘Planar polarity establishment is not highly sensitive to variation in protein levels of core complex components’.

Also added westerns and text/references showing that for the tested proteins there is a reduction in protein levels upon removal of one gene dosage in Results section ‘Planar polarity establishment is…’ and Fig.S2.

The data in Fig 5 are somewhat internally inconsistent, and inconsistent with the authors' interpretation. In both repolarization conditions, the authors claim that repolarization extends only to row 1, and row 1 is statistically different from non-repolarized row 1, but so too is row 3. Row 2 is not. This makes no sense, and suggests either that the statistical tests are inappropriate and/or the data is too sparse to be meaningful. 

As we’re sure the reviewer appreciates, this was an extremely complex experiment to perform and analyse. We spent a lot of time trying to find the best way to illustrate the results (finally settling on a 2D vector representation of polarity) and how to show the paired statistical comparisons between different groups. Moreover, in the end we were only able to detect generally quite modest (statistically significant) changes in cell polarity under the experimental conditions.

However, we note that failure to see large and consistent changes in polarity is exactly the expected result if it is hard to repolarise from a boundary – and this is of course the conclusion that we draw. Conversely, if repolarisation were easy, which was our expectation at least under de novo conditions without existing polarity, then we would have expected large and highly statistically significant changes in polarity across multiple cell rows. Hence we stand by our conclusion that ‘it is hard to repolarise from a boundary of Fz overexpression in both control and de novo polarity conditions’.

Overall, we were trying to establish three points:

(1) to demonstrate that repolarisation occurs from a boundary of overexpression i.e. from boundary 0 to row 0

(2) to establish whether a wave of repolarisation occurs across rows 1, 2 and 3

(3) to determine if in repolarisation in de novo condition it is easier to repolarise than in repolarisation in the control (already polarised) condition Taking each in turn:

(1) To detect repolarisation from a boundary relative to the control condition, we have to compare row 0 in repolarisation condition (Fig.5G,K) vs control condition (Fig.5F,J). This comparison shows a significative repolarisation (p=0.0014). From now, row 0 in repolarisation condition is our reference for repolarisation occurring.

(2) To determine if there is a wave of repolarisation in the repolarisation condition we have to compare row 0 vs row 1 to 3 in the repolarisation condition (Fig.5K). Row 1 is not significantly different to row 0, but rows 2 and 3 are different and the vectors show obviously lower polarity than row 0. Hence no wave of repolarisation is detected over rows 1 to 3.

(3) To determine if it is easier to repolarise in the de novo condition, our reference for establishment of a repolarisation pattern is the polarisation condition in rows 0 to 3. So, we compare repolarisation condition vs repolarisation in de novo condition, row 0 vs row 0, row 1 vs row 1, row 2 vs row 2 and row 3 vs row 3 – in each case no significative difference in polarity is detected, supporting our conclusion that it is not easier to repolarise in the de novo condition.

We agree that the variations in row 3 are puzzling, but there is no evidence that this is due to propagation of polarity from row 0, and so in terms of our three questions, it does not alter our conclusions.

Changes to manuscript: We have extensively revised the text describing the results in Fig.5 to hopefully make the reasons for our conclusions clearer and also be more cautious in our conclusions in Results section ‘Induced core protein relocalisation…’. 

For the related boundary intensity data in Fig 6, the authors need to describe exactly how boundaries were chosen or excluded from the analysis. Ideally, all boundaries would be classified as either meido-lateral (meaning anterior-posterior) or proximal-distal depending on angle. 

We thank the reviewer for pointing out that this was not clear.

All boundaries were classified following their orientation compared to the Fz over-expression boundary using hh-GAL4 expressed in the wing posterior compartment. Horizontal junctions were defined as parallel to the Fz over-expression boundary (between 0 and 45 degrees) and mediolateral junctions as junctions linking two horizontal boundaries (between 45 and 90 degrees).

Changes to manuscript: The boundary classification detailed above has been added in the Materials and Methods.

If the authors believe their Fig 5 and 6 analyses, how do they explain that hairs are reoriented well beyond where the core proteins are not? This would be a dramatic finding, because as far as I know, when core proteins are polarized, prehair orientation always follows the core protein distribution. Surprisingly, the authors do not so much as comment about this. The authors should age their wings just a bit more to see whether the prehair pattern looks more like the adult hair pattern or like that predicted by their protein orientation results.

Again the reviewer makes an interesting point, and we agree that this is something that we should have more directly addressed in the manuscript.

There are three reasons why we might expect adult trichomes to show a different effect from the measured core protein polarity pattern seen in our experiments:

(i) we are assaying core protein polarity at 28h APF, but trichomes emerge at >32h APF, so there is still time for polarity to propagate a bit further from the boundary. We now have added data showing that by the point of trichome initiation, the wave of polarisation extends 3-4 cell rows (Fig.S5A).

(ii) it has long been known that a strong localisation of core proteins at a cell edge is not required for polarisation of trichome polarity from a boundary. For instance, in Strutt & Strutt 2007 we show clones of cells overexpressing Fz causing propagation through pk[pk-sple] mutant tissue where there is no detectable core protein polarity. We were following up prior observations of Adler et al., 2000 in the wing and Lawrence et al., 2004 in the abdomen.

(iii) there is evidence to suggest that the polarity of adult trichomes is locally coupled, possibly mechanically. This point is hard to prove without live imaging taking in both initial core protein localisation, the site of actin-rich trichome initiation and then the final orientation of the much larger microtubule filled trichome, and we’re not aware that such data exist. However, Wong & Adler 1993 (JCB) showed that over a number of hours trichomes become much larger and move towards the centre of the cell, presumably becoming decoupled from any core protein cue. The images in Guild … & Tilney, 2005 (MBoC)  are also interesting to look at in this regard. Finally, septate junction proteins have been implicated in local alignment of trichomes, independently of the core pathway (Venema … & Auld, 2004 Dev Biol).

Changes to manuscript: Added new data in Fig.S5A showing where trichomes initiate under 6h de novo induction conditions, for comparison to core protein localisation and adult trichome data in Fig.5. Added some text explaining why adult trichome repolarisation might be stronger than the observed effects on core protein localisation in Discussion. 

Minor points:

As the authors know, there is a model in the literature that suggests microtubule trafficking provides a global cue to orient PCP. The authors' repolarization data in Fig 4 make a reasonably convincing case against a role for no role for microtubules in cell-scale signaling, but do not rule out a role as a global cue. The authors should be careful of language such as "...MTs and core proteins being oriented independently of each other" that would appear to possibly also refer to a role as a global cue. 

Thank you for pointing out that this was not clear. We have now modified the text to hopefully address this.

Changes to manuscript: Text updated in Results section ‘Microtubules do not provide…’.

Significance:

There are two negative conclusions and one positive conclusion made by the authors. Provided the above points are addressed, the negative conclusions, that core proteins are not limiting and that microtubules are not involved in cell-scale signaling are solid. The positive conclusion is more nebulous - the authors say that cell-scale signaling is strong relative to cell-cell signaling - but how strong is strong? Strong relative to their prior expectations? I'm not sure how to interpret such a conclusion. Overall, we learn something from these results, though it fails to reveal anything about mechanism. These results will be of some interest to those studying PCP.

The reviewer raises an interesting point, which is how do you compare the strength of two different processes, even if both processes affect the same outcome (in this case cell polarity). Repolarisation from a boundary has not been carefully studied at the level of core protein localisation in any previous study to our knowledge – this is one of the important novel aspects of this study. Hence there is not a baseline for defining strong repolarisation. Similarly, there has been no investigation of the nature of ‘cell-scale signalling’. This was a considerable challenge for us in writing the manuscript, and we have done our best to find appropriate language that hopefully conveys our message adequately. Minimally our work may provide a baseline for helping to define the ‘strengths’ of these processes in future studies.

One of our main points is that we can generate an artificial boundary of Fz expression, where Fz levels are at least several fold higher than in the neighbouring cell (e.g. compare Fig.4N’ and O’) and only two rows of cells show a significant change in polarity relative to controls. Even when the tissue next to the overexpression domain is still in the process of generating polarity (de novo condition) then the boundary has little effect on polarity in neighbouring cell rows. This was a result that surprised us, and we tried to convey that by using language to suggest cell-scale signalling was stronger than cell-cell signalling i.e. stronger in terms of the ability to define the final direction of polarity.

Changes to manuscript: In the revised manuscript we have reviewed our use of language and now avoid saying ‘strong’ but instead use terms such as ‘effective’ and ‘robust’ in e.g. Results section ‘Induced core protein relocalisation…’, the Discussion and we have also changed the title of the manuscript to avoid claiming a ‘strong’ signal.

Reviewer #2:

[…] Critique

The experiments described in this paper are of high quality with a sophisticated level of design and analysis. However, there needs to be some recalibration of the extent of the conclusions that can be drawn (see below). Moreover, a limitation of this paper is that, despite the quality of their data, they cannot give a molecular hint about the nature of their proposed cell-scale signal. Below are a two key points that the authors may want to clarify.

(1) The first set of repolarisation experiment is performed after the global cell rearrangements that have been shown to act as global signal. However, this approach does not exclude the possible contribution of an unknown diffusible global signal.

A similar point was raised by Reviewer 1. For the convenience of this reviewer, we’ll summarise the arguments against such an unknown cue again below. More broadly, both reviewers asking a similar question indicates that we have failed to lay out the evidence in sufficient detail. In our defence, we have used the same ‘de novo’ paradigm in three previous publications (Strutt and Strutt 2002, 2007; Brittle et al 2022) without attracting (overt) controversy. We have now added text to the Introduction and Results that goes into more detail, as well as more experimental evidence (Fig.S5).

Firstly, it is worth noting that the global cues acting in the wing are poorly understood, with mostly negative evidence against particular cues accruing in recent years. This makes it a hard subject to succinctly discuss. Secondly, we accept that it is hard to prove there is no influence of global cues, when the nature of those cues and the time at which they act remain unclear. Below we summarise the reasons why we believe there are not significance effects of global cues in our experiments that would influence the interpretation of our results.

First, our reading of the literature supports a broad consensus that an early radial core planar polarity pattern is realigned by cell flow produced by hinge contraction beginning at around 16h APF (e.g. Aigouy et al., 2010; Strutt and Strutt, 2015; Aw and Devenport, 2017; Butler and Wallingford, 2017; Tan and Strutt, 2025). Taken at face value, this suggests that there are ‘radial’ cues present prior to hinge contraction, maybe coming from the wing margin – arguably these radial cues could be Ft-Ds or Wnts or both, given they are expressed in patterns consistent with such a role (notwithstanding the published evidence arguing against roles for either of these cues). It then appears that hinge contraction supercedes these cues to convert a radial pattern to a proximodistal pattern – whether the radial cues that affect the core pathway earlier remain active after hinge contraction is unclear, although both Ft-Ds and Wnts appear to maintain their ‘radial’ patterns beyond the beginning of hinge contraction (e.g. Merkel et al., 2014; Ewen-Campen et al.,2020; Yu et al., 2020).

We think that the reviewers are proposing the presence of a proximodistal cue that is active in the proximal region of the wing that we use for our experiments shown e.g. in Fig.5, and that this cue orients core polarity here (but not elsewhere in the wing) in a time window after 18h APF. Ft-Ds and Wnts do not seem to be plausible candidates as they are still in ‘radial’ patterns. This leaves either an unknown proximodistal cue (a gradient of some unknown signalling molecule?), or possibly some ability of hinge contraction to align proximodistal polarity specifically in this wing region but not elsewhere. We cannot definitively rule out either of these possibilities, but neither do we think there is sufficient evidence to justify invoking their existence to explain our observations.

In particular, the reason that we don’t think there is a proximodistal cue in the proximal part of the wing after 18h APF, is that work from our lab shows that induction of Fz or Stbm expression at times around or after the start of hinge contraction (i.e. >16 h APF) results in increasing levels of trichome swirling with polarity not being coordinated with the tissue axis either proximally or distally (Strutt and Strutt, 2002; Strutt and Strutt 2007). Our simplest interpretation of this is that induction at these stages fails to result in the early radial pattern of core pathway polarity being established and hence a failure of hinge contraction to reorient radial to proximodistal. If hinge contraction alone could specify proximodistal polarity in the absence of the earlier radial polarity, then we would not expect to see swirling over much of the proximal wing (where the forces from hinge contraction are strongest, Etournay et al., 2015).

In this manuscript, our earliest de novo experiments begin at 18h APF (de novo 10h), then at 20h APF (de novo 8h) and at 22h APF (de novo 6h). The image in Fig. 5B referred to by Reviewer 1, is of a wing where Fz is induced de novo at 22 h APF. In these wings, as expected, the core proteins localise asymmetrically in stereotypical swirling patterns throughout the wing surface (see Fig. 2M and also Strutt and Strutt, 2002; Strutt and Strutt 2007), but – usefully for our experiments – they broadly localise along the proximal-distal axis in the region analysed in Fig. 5B. Given the strong swirling in surrounding regions when inducing at >20h APF, we feel reasonably confident in assuming that the pattern is not due to a proximodistal cue present in the proximal wing. We appreciate that the original manuscript did not show images including the trichome pattern in adjacent regions, so this point would not have been clear, but we now include these in Supplementary Fig.S5. We have also added a note in the legend to Fig. 5B to clarify that the proximodistal pattern seen is local to this wing region.

Changes to manuscript: Text extended in Introduction and Results to better explain why we believe the de novo conditions that we use most likely result in a polarity pattern that is not significantly influenced by ‘global cues’. Now show zoomed-out images of the surrounding region around the experiment region proximal to the anterior cross-vein region in adult wings, showing that the polarity pattern does not become more proximodistal when induction time is longer, and also that there is not overall proximodistal polarity in proximal regions of the wing, arguing against an unknown proximodistal polarity cue at these stages of development (Fig.S5B-E’’’).

(2) The putative non-local cell scale signal must be more precisely defined (maybe also given a better name). It is not clear to me that one can separate cell-scale from molecular-scale signal.

Local signals can redistribute within a cell (or membrane) so local signals are also cell-scale. Without a clear definition, it is difficult to interpret the results of the gene dosage experiments. The link between gene dosage and cell-scale signal is not rigorously stated. Related to this, the concluding statement of the introduction is too cryptic.

We thank the reviewer for raising this, as again a similar comment was made by Reviewer 1, so we are clearly falling short in defining the term. We have now had another attempt in the Introduction.

To more specifically answer the point made by the reviewer regarding molecular vs cellular, we are essentially being guided here by the prior computational modelling work, as at the biological level the details are still being worked out. A specific class of previous models only allowed ‘signals’ between core proteins to act ‘locally’, meaning within a cell junction, and within the models there was no explicit mechanism by which proteins on other junctions could ‘detect’ the polarity of a neighbouring junction (e.g. Amonlirdviman et al., 2005; Le Garrec et al., 2006; Fischer et al., 2013). Other models implicitly or explicitly encode a mechanism by which cell junctions can be influenced by the polarity of other junctions (e.g. Meinhardt, 2007; Burak and Shraiman, 2009; Abley et al., 2013; Shadkhoo and Mani, 2019), for instance by diffusion of a factor produced by localisation of particular planar polarity proteins.

We agree with the reviewer that a cell-scale signal will depend on ‘molecules’ and thus could be called ‘molecular-scale’, but here by ‘molecular-scale’ we mean signals that at the range of the sizes of molecules i.e. nanometers, rather than cell-scale signals that act at the size of cells i.e. micrometers. A caveat to our definition is that we implicitly include interactions that occur locally on cell junctions (<1 µm range) within ‘molecular-scale’, but this is a shorter range than ‘cellular-scale’ which requires signals acting over the diameter of a cell (3-5 µm). Nevertheless, we think the concept of ‘molecular-scale’ vs ‘cell-scale’ is a helpful one in this context, and have attempted to address the issue through a more careful definition of the terms.

Changes to manuscript: Text revised in Introduction and legend to Fig.1 to more carefully define ‘cell-scale signalling’ and to distinguish it from ‘molecular-scale signalling’. Final sentence of Introduction also altered so we no longer cryptically speculate on the nature of the cell-scale signal but leave this to the Discussion.

Minor comments. 

Some of the (clever) genetic manipulation may need more details in the text. For example:

- Need to specify if the hs-flp approach induces expression throughout the tissue.

We apologise for the lack of clarity. In all the experiments, the hs-FLP transgene is present in all cells, and heat-shock results in ubiquitous expression. 

Changes to manuscript: We have clarified this in the Results and Materials and Methods.

- Need to specify in the text that in the unpolarised condition the tissue is both dsh and fz mutant.

The reviewer is of course correct and we have updated this point in the text. The full genotype for the unpolarised condition is: w dsh¹ hsFLP22/y;; Act>>fz-mKate2sfGFP, fz^P21/fz^P21 (see Table S1). So this line is mutant for dsh and fz with induced expression of Fz-mKate2sfGFP. 

Changes to manuscript: We have clarified this in the relevant part of the Results.

- Need to specify in the text that the experiment illustrated in Fig 5 is with hh-gal4. 

As noted by the reviewer, we continued to use the same hh-GAL4 repolarisation paradigm as in Fig.4 and this info was in the legend to Fig.5 legend. However, we agree it is helpful to be explicit about this in the main text.

Changes to manuscript: We have added this to this section of the Results.

- Need to address a possible shortcoming of the hh experiment, that the AP boundary is a region of high tension.

It is true that the AP boundary is under high tension in the wing disc (e.g. Landsberg et al., 2009). But we are not aware of any evidence that this higher tension persists into the pupal wing. In separate studies we have labelled for Myosin II in pupal wings (Trinidad et al 2025 Curr Biol; Tan & Strutt 2025 Nature Comms), and as far as we have noticed have not seen preferentially higher levels on the AP boundary. We think if tension were higher, the cell boundaries would appear straighter than in surrounding cells (as seen in the wing disc) and this is not evident in our images.

- Need to dispel the possibility that there is no residual polarisation (e.g. of other components) in fz1 mutant (I assume this is the case).

We use the null allele fz[P21] through this work, and we and others have consistently reported a complete loss of polarisation of other core proteins or downstream components in this background. The caveat to this is that core proteins that persist at cell junctions always appear at least slightly punctate in mutant backgrounds for other core proteins, and so any automated detection algorithm will always find evidence of individual cell polarity above a baseline level of uniform distribution. Hence we tend to use lack of local coordination of polarity (variance of cell polarity angle) as an additional measure of loss of polarisation, in addition to direct measures of average cell polarity. (We discuss this in the QuantifyPolarity manuscript Tan et al 2021 e.g. Fig.S6).

Changes to manuscript: We now include in the Materials and Methods section ‘Fly genetics…’ a much more extensive explanation of the evidence for specific mutant alleles being ‘null’ for planar polarity function (including dsh1 as raised by Reviewer 1), specifically that they result in no detectable planar polarisation of either other core proteins or downstream effectors, and added appropriate references.

- Need to provide evidence that 50% gene dosage commensurately affect protein level. 

This is a good suggestion. In the case of Stbm, we have already published a western blot showing that a reduction in gene dosage results in reduced protein levels (Strutt et al 2016, Fig.S6). We have now performed western blots to quantify protein levels upon reduction of fmi, pk and dgo levels (we actually used EGFP-dgo for the latter, as we don’t have antibodies that can detect endogenous Dgo on western blots).

Changes to manuscript: When presenting the dosage reduction experiments, we now refer back to Strutt et al., 2016 explicitly for Stbm, and have added western blot data for Fmi, Pk and EGFPDgo in new Fig.S2.

- I am surprised that the relationship with microtubule polarity was never investigated. Is this true? 

We agree this is a point that needed further clarification, as Reviewer 1 made a related point regarding the two possible roles for microtubules, one being as a mediator of a global cue upstream of the core pathway, and the second (which we investigate in this manuscript) as a mediator of a cell-scale signal downstream of the core pathway.

Both the Uemura and Axelrod groups have published on potential upstream function as a global cue mediator in the Drosophila wing (e.g. Shimada et al., 2006; Harumoto et al., 2010; Matis et al., 2014).

Both groups have also looked out whether core pathway components could affect orientation of microtubules (Harumoto et al., 2010; Olofsson at al., 2014; Sharp and Axelrod 2016). Notably Harumoto et al., 2010 observed that in 24h APF wings, loss of Fz or Stbm did not alter microtubule polarity from a proximodistal orientation consistent with the microtubules aligning along the long cell axis in the absence of other cues. However, this did not rule out an instructive effect of Fz or Stbm on microtubule polarity during core pathway cell-scale signalling. The Axelrod lab manuscripts saw interesting effects of Pk protein isoforms on microtubule polarity, albeit not throughout the entire wing, which hinted at a potential role in cell-scale signalling. Taken together this prior work was the motivation for our directed experiments to specifically test whether the core pathway might generate cell-scale polarity by instructing microtubule polarity.

Changes to manuscript: We have revised the Results section ‘Microtubules do not…’ to make a clearer distinction regarding possible ‘upstream’ and ‘downstream’ roles of microtubules in Drosophila core pathway planar polarity and the motivation for our experiments investigating the latter.

- The authors suggest that polarity does not propagate as a wave. And yet the range measured in adult is longer than in the pupal wing. Explain. 

Again an excellent point, also made by Reviewer 1, which we have now addressed explicitly in the manuscript. For the convenience of this reviewer, we lay out the reasons why we think the propagation of polarity seen in the adult is further than seen for core protein localisation.

There are three reasons why we might expect adult trichomes to show a different effect from the measured core protein polarity pattern seen in our experiments:

(i) we are assaying core protein polarity at 28h APF, but trichomes emerge at >32h APF, so there is still time for polarity to propagate a bit further from the boundary. We now have added data showing that by the point of trichome initiation, the wave of polarisation extends 3-4 cell rows (Fig.S5A).  

(ii) it has long been known that a strong localisation of core proteins at a cell edge is not required for polarisation of trichome polarity from a boundary. For instance, in Strutt & Strutt 2007 we show clones of cells overexpressing Fz causing propagation through pk[pk-sple] mutant tissue where there is no detectable core protein polarity. We were following up prior observations of Adler et al 2000 in the wing and Lawrence et al 2004 in the abdomen.

(iii) there is evidence to suggest that the polarity of adult trichomes is locally coupled, possibly mechanically. This point is hard to prove without live imaging taking in both initial core protein localisation, the site of actin-rich trichome initiation and then the final orientation of the much larger microtubule filled trichome, and we’re not aware that such data exist. However, Wong & Adler 1993 (JCB) showed that over a number of hours trichomes become much larger and move towards the centre of the cell, presumably becoming decoupled from any core protein cue. The images in Guild … & Tilney, 2005 (MBoC)  are also interesting to look at in this regard. Finally, septate junction proteins have been implicated in local alignment of trichomes, independently of the core pathway (Venema … & Auld, 2004 Dev Biol).

Changes to manuscript: Added new data in Fig.S5A showing where trichomes initiate under 6h de novo induction conditions, for comparison to core protein localisation and adult trichome data in Fig.5. Added some text explaining why adult trichome repolarisation might be stronger than the observed effects on core protein localisation in Discussion. 

- The discussion states that the cell-intrinsic system remains to be fully characterised, implying that it has been partially characterised. What do we know about it? 

As the reviewer probably realises, we were attempting to side-step a long speculative discussion about the various hints and ideas in the literature by grouping them under the umbrella of ‘remaining to be fully characterised’. We would argue that this current manuscript is the first to attempt to systematically investigate the nature of ‘cell-scale signalling’. The lack of prior work is probably due to two factors (i) pioneering theoretical work showed that a sufficiently strong global signal coupled with ‘local’ (i.e. confined to one cell junction) protein interactions was sufficient to polarise cells without the need to invoke the existence of a cell-scale signal; (ii) there is no easy way to identify cell-scale signals as their loss results in loss of polarity which will also occur if other (i.e. more locally acting) core pathway functions are compromised.

The main investigation of the potential for cell-scale signalling has been another set of theory studies (Burak and Shraiman 2009; Abley et al., 2013; Shadkhoo and Mani 2019) which have considered the possibility of diffusible signals. In our present work we have further considered the possibility of a ‘depletion’ model, based on the pioneering theory work of Hans Meinhardt, and as discussed above the possibility that microtubules could mediate a cell-scale signal.

Changes to manuscript: We have revised the Discussion to hopefully be clearer about the current state of knowledge.

Reviewer #3:

[…] Major comments

The data are clearly presented and the manuscript is well written. The conclusions are well supported by the data. 

(1) The authors use a system to de novo establish PCP, which has the advantage of excluding global cues orienting PCP and thus to focus on the cell-intrinsic mechanisms. At the same time, the system has the limitation that it is unclear to what extent de novo PCP establishment reflects 'normal' cell scale PCP establishment, in particular because the Gal4/UAS expression system that is used to induce Fz expression will likely result in much higher Fz levels compared with the endogenous levels. The authors should briefly discuss this limitation. 

We apologise if this wasn’t clear. We only used GAL4/UAS overexpression when we were generating an artificial boundary of Fz expression with hh-GAL4 to induce repolarisation. The de novo induction system involves Fz::mKate2-sfGFP being expressed directly under an Act5C promoter without use of GAL4/UAS. In response to a comment from Reviewer 1 we have now carried out western blot analysis which shows that Fz::mKate2-sfGFP levels under Act5C are actually lower than endogenous Fz levels. As we achieve normal levels of polarity, similar to what we measure in wild-type conditions when measured using QuantifyPolarity, we assume that therefore Fz levels are not limiting under these conditions. However, we note that lower than normal levels of Fz might sensitise the system to perturbation, which in fact would be advantageous in our study, as it might for instance have been expected to more readily reveal dosage sensitivity of other components.

Changes to manuscript: We now describe the levels of expression achieved using the de novo induction system (Fig.S1C-D) and discuss possible consequences in the relevant Results sections and Discussion.

(2) Fig. 3. The authors use heterozygous mutant backgrounds to test the robustness of de novo PCP establishment towards (partial) depletion in core PCP proteins. The authors conclude that de novo polarization is 'extremely robust to variation in protein level'. Since the authors (presumably) lowered protein levels by 50%, this conclusion appears to be somewhat overstated. The authors should tune down their conclusion. 

Reviewer 1 makes a similar point about whether we can argue that the lack of sensitivity to a 50% reduction in protein levels actually rules out the depletion model. To address the comments of both reviewers we had now added some further narrative and caveats in the text.

We nevertheless believe that the experiments shown effectively make the point that there is no strong dosage sensitivity – and it remains our contention that if protein levels were the key to setting up cell-scale polarity, then a 50% reduction would be expected to show an effect on the rate of polarisation. We further note that as Fz::mKate2-sfGFP levels are lower than endogenous Fz levels, the system might be expected to be sensitised to further dosage reductions, and despite this we fail to see an effect on rate of polarisation.

In a similar vein, Reviewer 2 requested data on whether dosage reduction altered protein levels by the expected amount. We have now added further explanation/references and western blot data to address this.

Changes to manuscript: Added some narrative and caveats regarding whether lowering levels more than 50% would add to our findings in the Discussion. Revised conclusions to be more cautious including altering section title to read ‘Planar polarity establishment is not highly sensitive to variation in protein levels of core complex components.

Also added westerns and text/references showing that for the tested proteins there is a reduction in protein levels upon removal of one gene dosage in Results section ‘Planar polarity establishment is…’ and Fig.S2.

Minor comments :

(1) Page 3. The authors mention and reference that they used the PCA method to quantify cell polarity magnification and magnitude. It would help the unfamiliar reader, if the authors would briefly describe the principle of this method. 

Changes to manuscript: More details have been added in Materials & Methods.

Significance:

The manuscript contributes to our understanding of how planar cell polarity is established. It extends previous work by the authors (Strutt and Strutt, 2002,2007) that already showed that induction of core PCP pathway activity by itself is sufficient to induce de novo PCP. This manuscript further explores the underlying mechanisms. The authors test whether de novo PCP establishment depends on an 'inhibitory signal', as previously postulated (Meinhardt, 2007), but do not find evidence. They also test whether core PCP proteins help to orient microtubules (which could enhance cell intrinsic polarization of core PCP proteins), but, again, do not find evidence, corroborating previous work (Harumoto et al, 2010). The most significant finding of this manuscript, perhaps, is the observation that local de novo PCP establishment does not propagate far through the tissue. A limitation of the study is that the mechanisms establishing intrinsic cell scale polarity remain unknown. The work will likely be of interest to specialists in the field of PCP.

eLife assessment

This important study provides novel evidence that navigational experiences can shape perceptual scene representations. The evidence presented is incomplete and would benefit from clearer explanations of the experiment design and careful discussion of alternative interpretations such as contextual associations or familiarity. The work will be of interest to cognitive psychologists and neuroscientists working on perception and navigation.

[Editors’ note: A revised version of this work has been published in the Journal of Cognitive Neuroscience (DOI: https://doi.org/10.1162/JOCN.a.2409).]

Reviewer #1 (Public Review):

In this study, Li et al. aim to determine the effect of navigational experience on visual representations of scenes. Participants first learn to navigate within simple virtual environments where navigation is either unrestricted or restricted by an invisible wall. Environments are matched in terms of their spatial layout and instead differ primarily in terms of their background visual features. In a later same/different task, participants are slower to distinguish between pairs of scenes taken from the same navigation condition (i.e. both restricted or both unrestricted) than different navigation conditions. Neural response patterns in the PPA also discriminate between scenes from different navigation conditions. These results suggest that navigational experience influences perceptual representations of scenes. This is an interesting study, and the results and conclusions are clearly explained and easy to follow. There are a few points that I think would benefit from further consideration or elaboration from the authors, which I detail below.

First, I am a little sceptical of the extent to which the tasks are able to measure navigational or perceptual experience with the scenes. The training procedure seems like it wouldn't require obtaining substantial navigational experience as the environments are all relatively simple and only require participants to follow basic paths, rather than encouraging more active exploration of a more complex environment. Furthermore, in the same/different task, all images show the same view of the environment (meaning they show the exact same image in the "same environment" condition). The task is therefore really a simple image-matching task and doesn't require participants to meaningfully extract the perceptual or spatial features of the scenes. An alternative would have been to present different views of the scenes, which would have prevented the use of image-matching and encouraged further engagement with the scenes themselves. Ultimately, the authors do still find a response time difference between the navigation conditions, but the effect does appear quite small. I wonder if the design choices could be obscuring larger effects, which might have been better evident if the navigational and perceptual tasks had encouraged greater encoding of the spatial and perceptual features of the environment. I think it would be helpful for the authors to explain their reasons for not employing such designs, or to at least give some consideration to alternative designs.

Figure 1B illustrates that the non-navigable condition includes a more complicated environment than the navigable condition, and requires following a longer path with more turns in it. I guess this is a necessary consequence of the experiment design, as the non-navigable condition requires participants to turn around and find an alternative route. Still, this does introduce spatial and perceptual differences between the two navigation conditions, which could be a confounding factor. What do the response times for the "matched" condition in the same/different task look like if they are broken down by the navigable and non-navigable environments? If there is a substantial difference between them, it could be that this is driving the difference between the matched and mismatched conditions, rather than the matching/mismatching experience itself.

In both experiments, the authors determined their sample sizes via a priori power analyses. This is good, but a bit more detail on these analyses would be helpful. How were the effect sizes estimated? The authors say it was based on other studies with similar methodologies - does this mean the effect sizes were obtained from a literature search? If so, it would be good to give some details of the studies included in this search, and how the effect size was obtained from these (e.g., it is generally recommended to take a lower bound over studies). Or is the effect size based on standard guidelines (e.g., Cohen's d ≈ 0.5 is a medium effect size)? If so, why are the effect sizes different for the two studies?

Reviewer #2 (Public Review):

Summary:

Li and colleagues applied virtual reality (VR) based training to create different navigational experiences for a set of visually similar scenes. They found that participants were better at visually discriminating scenes with different navigational experiences compared to scenes with similar navigational experiences. Moreover, this experience-based effect was also reflected in the fMRI data, with the PPA showing higher discriminability for scenes with different navigational experiences. Together, their results suggest that previous navigational experiences shape visual scene representation.

Strengths:

(1) The work has theoretical value as it provides novel evidence to the ongoing debate between visual and non-visual contributions to scene representation. While the idea that visual scene representation can encode navigational affordances is not new (e.g., Bonner & Epstein, 2017, PNAS), this study is one of the first to demonstrate that navigational experiences can causally shape visual scene representation. Thus, it serves as a strong test for the hypothesis that our visual scene representations involve encoding top-down navigational information.

(2) The training paradigm with VR is novel and has the potential to be used by the broader community to explore the impact of experience on other categorical visual representations.

(3) The converging evidence from behavioral and fMRI experiments consolidates the work's conclusion.

Weaknesses:

(1) While this work attempts to demonstrate the effect of navigational experience on visual scene representation, it's not immediately clear to what extent such an effect necessarily reflects altered visual representations. Given that scenes in the navigable condition were more explored and had distinct contextual associations than scenes in the non-navigable condition (where participants simply turned around), could the shorter response time for a scene pair with mismatched navigability be explained by the facilitation of different contextual associations or scene familiarities, rather than changes in perceptual representations? Especially when the visual similarity of the scenes was high and different visual cues might not have been immediately available to participants, the different contextual associations and/or familiarity could serve as indirect cues to facilitate participants' judgment, even if perceptual representations remained intact.

(2) Similarly, the above-chance fMRI classification results in the PPA could also be explained by the different contextual associations and/or scene familiarities between navigable and non-navigable scenes, rather than different perceptual processes related to scene identification.

(3) For the fMRI results, the specificity of the experience effect on the PPA is not strictly established, making the statement "such top-down effect was unique to the PPA" groundless. A significant interaction between navigational conditions and ROIs would be required to make such a claim.

(4) For the behavioral results, the p-value of the interaction between groups and the navigational conditions was 0.05. I think this is not a convincing p-value to rule out visual confounding for the training group. Moreover, from Figure 2B, there appears to be an outlier participant in the control group who deviates dramatically from the rest of the participants. If this outlier is excluded, will the interaction become even less significant?

(5) Experiment 1 only consists of 25 participants in each group. This is quite a small sample size for behavioral studies when there's no replication. It would be more convincing if an independent pre-registered replication study with a larger sample size could be conducted.

Author response:

The final and revised version of this Reviewed Preprint has been published in the Journal of Cognitive Neuroscience. Please find the link to the final version below:

J Cogn Neurosci 2025; doi: https://doi.org/10.1162/JOCN.a.2409

eLife Assessment

The reviewers have found that this manuscript is a valuable contribution, and the evidence in support of its conclusions is mostly solid. It provides novel insights and raises interesting possibilities about the functions of an understudied histone modification within the nucleosome core; however, the data are mostly descriptive and correlative, and although this has value, it is not totally persuasive. Short of additional non-genomic experiments, a more detailed analysis of the genomic data and perhaps additional data would strengthen the conclusions. The manuscript crucially needs further antibody validation to raise confidence in the data.

Reviewer #1 (Public review):

Summary:

The authors investigate the role of H3K115ac in mouse embryonic stem cells. They report that H3K115ac localizes to regions enriched for fragile nucleosomes, CpG islands, and enhancers, and that it correlates with transcriptional activity. These findings suggest a potential role for this globular domain modification in nucleosome dynamics and gene regulation. If robust, these observations would expand our understanding of how non-tail histone modifications contribute to chromatin accessibility and transcriptional control.

Strengths:

(1) The study addresses a histone PTM in the globular domain, which is relatively unexplored compared to tail modifications.

(2) The implication of a histone PTM in fragile nucleosome localization is novel and, if substantiated, could represent a significant advance for the field.

Weaknesses:

(1) The absence of replicate paired-end datasets limits confidence in peak localization.

(2) The analyses are primarily correlative, making it difficult to fully assess robustness or to support strong mechanistic conclusions.

(3) Some claims (e.g., specificity for CpG islands, "dynamic" regulation during differentiation) are not fully supported by the analyses as presented.

(4) Overall, the study introduces an intriguing new angle on globular PTMs, but additional rigor and mechanistic evidence are needed to substantiate the conclusions.

Reviewer #2 (Public review):

Summary:

Kumar et al. aimed to assess the role of the understudied H3K115 acetylation mark, which is located in the nucleosomal core. To this end, the authors performed ChIP-seq experiments of H3K115ac in mouse embryonic stem cells as well as during differentiation into neuronal progenitor cells. Subsequent bioinformatic analyses revealed an association of H3K115ac with fragile nucleosomes at CpG island promoters, as well as with enhancers and CTCF binding sites. This is an interesting study, which provides important novel insights into the potential function of H3K115ac. However, the study is mainly descriptive, and functional experiments are missing.

Strengths:

(1) The authors present the first genome-wide profiling of H3K115ac and link this poorly characterized modification to fragile nucleosomes, CpG island promoters, enhancers, and CTCF binding sites.

(2) The study provides a valuable descriptive resource and raises intriguing hypotheses about the role of H3K115ac in chromatin regulation.

(3) The breadth of the bioinformatic analyses adds to the value of the dataset

Weaknesses:

(1) I am not fully convinced about the specificity of the antibody. Although the experiment in Figure S1A shows a specific binding to H3K115ac-modified peptides compared to unmodified peptides, the authors do not show any experiment that shows that the antibody does not bind to unrelated proteins. Thus, a Western of a nuclear extract or the chromatin fraction would be critical to show. Also, peptide competition using the H3K115ac peptide to block the antibody may be good to further support the specificity of the antibody. Also, I don't understand the experiment in Figure S1B. What does it tell us when the H3K115ac histone mark itself is missing? The KLF4 promoter does not appear to be a suitable positive control, given that hundreds of proteins/histone modifications are likely present at this region.

It is important to clearly demonstrate that the antibody exclusively recognizes H3K115ac, given that the conclusion of the manuscript strongly depends on the reliability of the obtained ChIP-Seq data.

(2) The association of H3K115ac with fragile nucleosomes based on MNase-Sensitivity and fragment length, which are indirect methods and can have technical bias. Experiments that support that the H3K115ac modified nucleosomes are indeed more fragile are missing.

(3) The comparison of H3K115ac with H3K122ac and H3K64ac relies on publicly available datasets. Since the authors argue that these marks are distinct, data generated under identical experimental conditions would be more convincing. At a minimum, the limitations of using external datasets should be discussed.

(4) The enrichment of H3K115ac at enhancers and CTCF binding sites is notable but remains descriptive. It would be interesting to clarify whether H3K115ac actively influences transcription factor/CTCF binding or is a downstream correlate.

(5) No information is provided about how H3K115ac may be deposited/removed. Without this information, it is difficult to place this modification into established chromatin regulatory pathways.

At the very least, the authors should acknowledge these limitations and provide additional validation of antibody specificity.

Reviewer #3 (Public review):

Summary:

Kumar et al. examine the H3K115 epigenetic mark located on the lateral surface of the histone core domain and present evidence that it may serve as a marker enriched at transcription start sites (TSSs) of active CpG island promoters and at polycomb-repressed promoters. They also note enrichment of the H3K115ac mark is found on fragile nucleosomes within nucleosome-depleted regions, on active enhancers, and CTCF-bound sites. They propose that these observations suggest that H3K115ac contributes to nucleosome destabilization and so may serve as a marker of functionally important regulatory elements in mammalian genomes.

Strengths:

The authors present novel observations suggesting that acetylation of a histone residue in a core (versus on a histone tail) domain may serve a functional role in promoting transcription, in CPG islands and polycomb-repressed promoters. They present a solid amount of confirmatory in silico data using appropriate methodology that supports the idea that the H3K115ac mark may function to destabilize nucleosomes and contribute to regulating ESC differentiation.

Weaknesses:

Additional experiments to confirm antibody specificity are needed. The authors use synthetic peptides for other markers (e.g., H3K122) to support the claim that the antibody is specific, but ChIP-ChIP assays are performed under cross-linked, non-denatured conditions, which preserve structure and epitope accessibility differently than synthetic peptides used for dot blots. Does the antibody give a single band in western blots of histones, and can the H3K115ac peptide block western and immunofluorescence signals of the antibody? Given that the antibody is a rabbit polyclonal, specificity is not a trivial consideration.

Author response:

Reviewer 1:

Comment 1. The reviewer was under the impression that that we did not perform biological replicates of our ChIP-seq experiments. All ChIP-seq (and ATAC-seq) experiments were performed with biological replicates and the Pearson’s correlations (all >0.9) between replicates were provided in Supplementary Table 1. We had indicated this in the text and methods but will try to make this even clearer.

Reviewer 2:

Comment 2. The reviewer states that our claim of H3K115ac being associated with fragile nucleosomes is based solely on MNase sensitivity and fragment length. This is not correct. Figure 3C and D show the results of sucrose gradient sedimentation experiments, followed by ChIP-seq clearly showing that H3K115ac fractionates with chromatin particles that are enriched for fragile nucleosomes and subnucleosomes. By contrast, H3K115ac is not enriched in stable mononucleosome

Comment 3. The reviewer states that our H3K122ac and H3K64ac comparison rely on publicly available datasets. We would emphasize that these are our own datasets generated and published previously (Pradeepa et. al., 2016) but using exactly the same native MNase ChIP protocol as used here for H3K115ac and processed with identical computational pipelines.

Reviewer 3:

Reviewer 3 is mistaken in thinking our ChIP experiments are performed under cross-linked conditions. As clearly stated in the main text and methods, all our ChIP-seq for histone modifications is done on native MNase-digested chromatin – with no cross-linking. This includes the spike-in experiment shown in Fig S1B to test H3K115ac antibody specificity against the bar-coded SNAP-ChIP® K-AcylStat Panel from Epicypher. We could not include H3K115ac bar-coded nucleosomes in that experiment since they are not available in the panel. 

Following that, we would propose to make minor revisions in response to specific reviewer recommendations before posting a version of record. These would include:

(1) Figure 2: title needs change: "H3K115ac marks CpG island promoters poised for activation". this is to make sure it reads with the title for the corresponding section in the main text. Also see: Reviewer 1 comment 7 in Recommendations part. 

(2) Figure S2B: legend should read: "Gene ontology analysis for the set of genes analysed in Figure 2C"

(3) Figure F4D: Provide the replicates for western blot 

(4) Figure 4A,B: Corrected formatting issues.

eLife Assessment

This study provides fundamental insights into eukaryotic phosphate homeostasis by demonstrating how yeast vacuoles dynamically regulate cytosolic phosphate levels. The conclusions are convincing, supported by an elegant combination of in vitro assays and in vivo measurements. This study will be of interest to cell biologists, particularly for those who are working in the field of phosphate metabolism.

Reviewer #1 (Public review):

The manuscript by Bru et al. focuses on the role of vacuoles as a phosphate buffering system for yeast cells. The authors describe here the crosstalk between the vacuole and the cytosol using a combination of in vitro analyses of vacuoles and in vivo assays. They show that the luminal polyphosphatases of the vacuole can hydrolyze polyphosphates to generate inorganic phosphate, yet they are inhibited by high concentrations. This balances the synthesis of polyphosphates against the inorganic phosphate pool. Their data further show that the Pho91 transporter provides a valve for the cytosol as it gets activated by a decline in inositol pyrophosphate levels. The authors thus demonstrate how the vacuole functions as a phosphate buffering system to maintain a constant cytosolic inorganic phosphate pool.

This is a very consistent and well-written manuscript with a number of convincing experiments, where the authors use isolated vacuoles and cellular read-out systems to demonstrate the interplay of polyphosphate synthesis, hydrolysis, and release. The beauty of this system the authors present is the clear correlation between product inhibition and the role of Pho91 as a valve to release Pi to the cytosol to replenish the cytosolic pool. I find the paper overall an excellent fit.

Comments on Revision:

The authors have addressed all my concerns.

Reviewer #3 (Public review):

Bru et al. investigated how inorganic phosphate (Pi) is buffered in cells using S. cerevisiae as a model. Pi is stored in cells in the form of polyphosphates in acidocalcisomes. In S. cerevisiae, the vacuole, which is the yeast lysosome, also fulfills the function of Pi storage organelle. Therefore, yeast is an ideal system to study Pi storage and mobilization.

They can recapitulate in their previously established system, using isolated yeast vacuoles, findings from their own and other groups. They integrate the available data and propose a working model of feedback loops to control the level of Pi on the cellular level.

This is a solid study, in which the biological significance of their findings is not entirely clear. The data analysis and statistical significance need to be improved and included, respectively. The manuscript would have benefited from rigorously testing the model, which would also have increased the impact of the study.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review): 

The manuscript by Bru et al. focuses on the role of vacuoles as a phosphate buffering system for yeast cells. The authors describe here the crosstalk between the vacuole and the cytosol using a combination of in vitro analyses of vacuoles and in vivo assays. They show that the luminal polyphosphatases of the vacuole can hydrolyse polyphosphates to generate inorganic phosphate, yet they are inhibited by high

concentrations. This balances the synthesis of polyphosphates against the inorganic phosphate pool. Their data further show that the Pho91 transporter provides a valve for the cytosol as it gets activated by a decline in inositol pyrophosphate levels. The authors thus demonstrate how the vacuole functions as a phosphate buffering system to maintain a constant cytosolic inorganic phosphate pool. 

This is a very consistent and well-written manuscript with a number of convincing experiments, where the authors use isolated vacuoles and cellular read-out systems to demonstrate the interplay of polyphosphate synthesis, hydrolysis, and release. The beauty of this system the authors present is the clear correlation between product inhibition and the role of Pho91 as a valve to release Pi to the cytosol to replenish the cytosolic pool. I find the paper overall an excellent fit and only have a few issues, including: 

(1) Figure 3: The authors use in their assays 1 mM ZnCl2 or 1mM MgCl2. Is this concentration in the range of the vacuolar luminal ion concentration? Did they also test the effect of Ca2+, as this ion is also highly concentrated in the lumen? 

The concentrations inside vacuoles reach those values. However, given that polyP can chelate divalent metal ions, what would matter are the concentrations of free Zn²⁺ or Mg²⁺ inside the organelle. These are not known. This is not critical since we use those two conditions only as a convenient tool to differentiate Ppn1 and Ppn2 activity in vitro. In our initial characterisation of Ppn2 (10.1242/jcs.201061), we had also tested Mn, Co, Ca, Ni, Cu. Only Zn and Co supported activity. Ca did not. Andreeva et al. (10.1016/j.biochi.2019.06.001) reached similar conclusions and extended our results.

(2) Regarding the concentration of 30 mM K-PI, did the authors also use higher and lower concentrations? I agree that there is inhibition by 30 mM, but they cannot derive conclusions on the luminal concentration if they use just one in their assay. A titration is necessary here. 

The concentration of 30 mM was not chosen arbitrarily. It is the luminal Pⁱ concentration that the vacuoles reached through polyP synthesis and hydrolysis when they entered a plateau of luminal Pⁱ. We consider this as an upper limit because polyP kept increasing which luminal Pⁱ did not. Thus, there is no physiological motivation for trying higher values. We have nevertheless added a titration to the revised version (new Fig. 3A).

(3) What are the consequences on vacuole morphology if the cells lack Pho91? 

We had not observed significant abnormalities during a screen of the genome-wide deletion collection of yeast (10.1371/journal.pone.0054160), nor in other experiments with pho91 mutants, which we have not included in this manuscript due to a lack of effect.

(4) Discussion: The authors do not refer to the effect of calcium, even though I would expect that the levels of the counterion should affect the phosphate metabolism. I would appreciate it if they would extend their discussion accordingly. 

The situation is much more complex because Ca2+ is not the only counterion. Major pools of counterions (up to hundreds of mM) are constituted by vacuolar lysine, arginine, polyamines, Mg, Zn etc. Their interplay with polyP is probably complex and worth to be treated in a dedicated project. If we wanted to limit the discussion of this complexity not to the simple statement that it is not understood, which is not very useful, we would have to engage in a lot of speculation. We feel that this would make the discussion lose focus and not contribute concrete insights.

(5) I would appreciate a brief discussion on how phosphate sensing and control are done in human cells. Do they use a similar lysosomal buffer system? 

Mammalian cells have their Pi exporter XPR1 mainly on a lysosome-like compartment (10.1016/j.celrep.2024.114316). Whether and how it functions there for Pi export from the cytosol is not entirely clear. We have addressed this situation in the revised discussion section.

Reviewer #2 (Public review): 

Summary: 

This manuscript presents a well-conceived and concise study that significantly advances our understanding of polyphosphate (polyP) metabolism and its role in cytosolic phosphate (Pi) homeostasis in a model unicellular eukaryote. The authors provide evidence that yeast vacuoles function as dynamic regulatory buffers for Pi homeostasis, integrating polyP synthesis, storage, and hydrolysis in response to cellular metabolic demands. The work is methodologically sound and offers valuable insights into the conserved mechanisms of phosphate regulation across eukaryotes. 

Strengths: 

The results demonstrate that the vacuolar transporter chaperone (VTC) complex, in conjunction with luminal polyphosphatases (Ppn1/Ppn2) and the Pi exporter Pho91, establishes a finely tuned feedback system that balances cytosolic Pi levels. Under Pi-replete conditions, inositol pyrophosphates (InsPPs) promote polyP synthesis and storage while inhibiting polyP hydrolysis, leading to vacuolar Pi accumulation. 

Conversely, Pi scarcity triggers InsPP depletion, activating Pho91-mediated Pi export and polyP mobilization to sustain cytosolic phosphate levels. This regulatory circuit ensures metabolic flexibility, particularly during critical processes such as glycolysis, nucleotide synthesis, and cell cycle progression, where phosphate demand fluctuates dramatically. 

From my viewpoint, one of the most important findings is the demonstration that vacuoles act as a rapidly accessible Pi reservoir, capable of switching between storage (as polyP) and release (as free Pi) in response to metabolic cues. The energetic cost of polyP synthesis-driven by ATP and the vacuolar proton gradient-highlights the evolutionary importance of this buffering system. The study also draws parallels between yeast vacuoles and acidocalcisomes in other eukaryotes, such as Trypanosoma and Chlamydomonas, suggesting a conserved role for these organelles in phosphate homeostasis. 

Weaknesses: 

While the manuscript is highly insightful, referring to yeast vacuoles as "acidocalcisome-like" may warrant further discussion. Canonical acidocalcisomes are structurally and chemically distinct (e.g., electrondense, in most cases spherical, and not routinely subjected to morphological changes, and enriched with specific ions), whereas yeast vacuoles have well-established roles beyond phosphate storage. A comment on this terminology could strengthen the comparative analysis and avoid potential confusion in the field.  

Yeast vacuoles show all major chemical features of acidocalcisomes. They are acidified, contain high concentrations of Ca, polyP (which make them electron-dense, too), other divalent ions, such as Mg, Zn, Mn etc, and high concentrations of basic amino acids. Thus, they clearly have an acidocalcisome-like character. In addition, they have hydrolytic, lysosomelike functions and, depending on the strain background, they can be larger than acidocalcisomes described e.g. in protists. We have elaborated on this point in the introduction of the revised version.

Reviewer #3 (Public review): 

Bru et al. investigated how inorganic phosphate (Pi) is buffered in cells using S. cerevisiae as a model. Pi is stored in cells in the form of polyphosphates in acidocalcisomes. In S. cerevisiae, the vacuole, which is the yeast lysosome, also fulfills the function of Pi storage organelle. Therefore, yeast is an ideal system to study Pi storage and mobilization. 

They can recapitulate in their previously established system, using isolated yeast vacuoles, findings from their own and other groups. They integrate the available data and propose a working model of feedback loops to control the level of Pi on the cellular level. 

This is a solid study, in which the biological significance of their findings is not entirely clear. The data analysis and statistical significance need to be improved and included, respectively. The manuscript would have benefited from rigorously testing the model, which would also have increased the impact of the study. 

It is not clear to us what the reviewer would see as a more rigorous test of the model.  

Reviewer #1 (Recommendations for the authors): 

(1) Figure 2: Why do the authors label the blue curve in A and B as BY and in C and D as WT? Is this a different genetic background they used here? This should be specified in the legend. 

No, it is the same background. The figures had been reshuffled before submission and we overlooked to replace "BY" by "WT". This has been corrected. Now we consistently use WT in all figures

(2) Figure 4 has different scaling for the two panels, which should be labeled as A and B. I am aware that the authors do this for comparison, but it is rather confusing at first glance. I recommend having them at the same scale. 

We chose this representation on two separate scales because this figure shall primarily illustrate that the shift between pho91 and WT curves vanishes in the presence of IP7. We now highlight in the figure legend that the scales are different to avoid confusion.  

(3) Figure 8: I would appreciate a model with normal and low Pi concentrations in comparison, as this is what the authors worked out. 

We have modified the figure. It now compares Pi-rich and Pi-limited scenarios.

(4) Minor issue: Wouldn't it make more sense to show the molar concentration in the Figures rather than the nmol of Pi/ug of protein? I am aware that this would require information on the vacuole volume rather than the reaction volume, and the authors do this calculation later on. 

It depends. We often chose this representation because it illustrates the price to pay (metabolic input in terms of protein that must be dedicated to this task) to sequester a certain quantity of Pⁱ. But, as we provide the corresponding Pⁱ concentration in the text, this information is accessible to the reader, too.

Reviewer #2 (Recommendations for the authors): 

As stated above in the weaknesses section, while functional parallels exist, canonical acidocalcisomes are structurally and chemically distinct, typically smaller, electron-dense, and enriched with cations. Whereas yeast vacuoles are larger, multifunctional organelles with well-established roles beyond phosphate storage. Explicitly addressing these differences would strengthen the comparative framework and prevent potential confusion in interpreting the evolutionary relationships between these organelles. 

We agree to some degree, which is the reason why we refer to vacuoles as acidocalcisome-like organelles. In fact, vacuoles share virtually all defining chemical traits of acidocalcisomes. They just have a second functional domain as hydrolytic, lysosome-like organelles. Given the plasticity of endo-lysosomal compartments, and acidocalcisomes belong to this group because of their biogenesis through the AP3 pathway, this is not shocking to us. But the reviewer's comment made us realize that it is better to explicitly address this point. We have added a section to the introduction to do this.

Reviewer #3 (Recommendations for the authors): 

(1) Page 8: It is unclear why the authors only estimated the Pi concentration in wild-type vacuoles. This should also be done for vacuoles from other strains. 

This information is inherent in Figure 2. PolyP hyperaccumulating strains show the same plateau as the wildtype, meaning that they also reach around 30 mM luminal Pi concentration, whereas vtc4 vacuoles reach only around 1/10th of that increase, indicating that they remain at 3 mM. We mention this now in the text.

(2) The attempts of the localization of Pho91 through tagging are not satisfactory. The author described different localizations for Pho91 depending on whether it was tagged on the N- or C-terminus or when Nterminally tagged and overexpressed using two strong promoters. While it is not uncommon that proteins show different localization patterns, depending on where the tag is inserted, it is possible that one of the tags would reflect the localization of the endogenous protein. There is an easy way to test this, in particular when Pho91 is endogenously tagged. pho91∆ has reported phenotypes such as abnormal vacuolar morphology or increased autophagy. They could also measure PI content in vacuoles. The authors could compare the phenotypes of the endogenously tagged strains with WT and a pho91∆ strain. 

Indeed, the attempts to localise the protein through fluorescent tags are unsatisfactory, in our hands as in the hands of others. We would not have created a series of many different tagged versions (we present only a selection of these in the manuscript) if the creation of a faithful reporter for Pho91 localisation were so straightforward. Expression from the endogenous promoter yields quite low signals (which is why others have overexpressed their GFP fusion from strong promotors). But overexpression brings at least a significant part of the protein to the cell surface, where it can then function as Pi importer and suffice to restore much of the maximal Pi uptake capacity that genuine plasma membrane transporters provide and support normal growth of the cells (Wykoff & O’Shea, 2001). But the localisation pattern of Pho91-GFP, likewise overexpressed from a strong promotor, does not reflect this plasma membrane localisation (see the references that the reviewer mentioned under (3)). The published overexpressed GFP-fusions localise only to the vacuole, suggesting that even in this case the GFP tag may create an artefact. Therefore, we went through a large variety of Pho91 gene fusions, which led us to the conclusion that the protein is very sensitive to tags at both ends and that fusion proteins hence are unlikely to reliably report the correct location of the protein. Given this, we resorted to quantitative proteomics to clarify the issue. This quantitative experiment goes beyond previously published proteomics analyses that the reviewer mentions under (3), which found the protein in the vacuolar fraction but did not calculate the enrichment factors, which is crucial. 

A strong phenotype of abnormal vacuolar morphology is not apparent in our cultures. 

(3) Moreover, Pho91 has been identified as a component enriched in vacuolar-mitochondria contact sites (vCLAMP), and this localization was confirmed with GFP-Pho91 (PMID: 25026036). Likewise, PMID: 35175277 also detected Pho91 by mass spectrometry as a vacuolar protein and showed endogenously tagged GFP-Pho91 on the vacuole (co-staining with Vph1). The authors may request the strains from the authors of these papers and use them for their experiments. PMID: 17804816, the oldest of the three reports (from 2007) reports a GFP-Pho91 under either TEF or ADH promoter that localizes to the vacuole. They also showed that the fusion protein is functional. These and other experiments led them to conclude that Pho91 exports phosphate from the vacuolar lumen to the cytoplasma. 

We have now included these references. As argued above, we have analysed also the strains from PMID17804816. The observed clear localisation of the fusion protein to vacuoles is only visible upon overexpression, not upon expression from the endogenous locus. Apparently also this construct is unlikely to report Pho91 localisation reliably (though, by chance, overexpression leads it to the correct location). Thus, we maintain our conclusion that C- or N-terminally GFP-tagged versions of Pho91 are unreliable tools for localising the protein.

(4) The impact of pho91∆ on Pho4-GFP nuclear localization is modest at best (increase from 5% of cells showing Pho4-GFP in the nucleus in WT vs 10% in pho91∆), and only somewhat stronger in ppn1∆/ppn2∆. This means 90% of pho91∆ cells do not respond, and Pho4-GFP stays cytoplasmic. It is unclear how the author can derive a meaningful conclusion from these data. Moreover, are these data really supporting the model, or do these data rather indicate that there are additional factors/pathways needed? What is the biological significance of the marginal increase from 5% to 10% of cells that would respond? What happens to the cells that cannot respond? Will they die or at least have a growth disadvantage? It would be useful to provide some functional studies. 

We should have explained the nature of the assay better. The experiment exploits the fact that dividing yeast cells transiently fall into a state of Pi scarcity during S-phase. Since S-phase is less than a quarter of the cell cycle, only a small fraction of the cells transiently activates the PHO pathway. These cannot be well characterised by ensemble assays, but microscopy circumvents this background of the whole population and picks them up very clearly, allowing to quantify them. We have adapted the respective chapter in the results section to improve the description of this experiment.

(5) The quantification of the data is suboptimal, as in most assays the mean and standard error of the mean (SEM) are given. SEM is not really appropriate in these cases because it gives only the error of the mean and not of the entire data. Therefore, the standard deviation (SD) is needed, which reports on the variability of the data, and which is usually much larger than the SEM. Using the SD, would also allow the authors to do proper statistical analysis, which is missing entirely in this manuscript. 

SEM also comprises the variability of the data. It is linked with the SD (SEM=SD/SQRT(n)), but SEM also considers the number of the experiments n. The main goal is to compare the means, and SEM is an appropriate and frequently used tool for this because it illustrates how well the arithmetic mean may estimate the true mean of the population. Therefore, we kept the SEM but have added tests of significance for the differences shown.

(6) Statistical testing in Figure 7 is essential as the effects are very small. Again, are these changes big enough for a biologically meaningful response? The authors should at least discuss this. 

Our previous time course analyses of InsPP dynamics, performed under comparable conditions as in this study, showed that InsP8 decreases by around 50% in the first 30 min after transfer to Pi starvation (DOI: https://doi.org/10.7554/eLife.87956) and that this decline is already sufficient to trigger the PHO starvation program, as assessed by Pho4-GFP translocation into the nucleus. Thus, a 50% decrease, which is observed in ppn1 ppn2 mutants, is functionally significant. We have now also evaluated statistical significance in Fig. 7, which is given for the 50% reduction of InsP8 and 1-InsP7 in ppn1 ppn2. 

Minor points: 

(1) There are a number of smaller edits (use of italic or better the absence thereof, lacking information in the reference list, and some typos). 

Thank you. We have corrected those.

(2) The exact n should be given in the Figure legend. 

Corrected.

(3) Page 8, line 8: it would be nice to have a picture of the wild-type vacuoles and what you measured. 

We now present a sample image in the new Suppl. Fig. 1.

(4) PMID: 11779791 showed already that Pho91 cannot rescue the absence of the plasma membrane Pi transporters. This study should be at least cited. 

This is not quite correct. The study that the reviewer mentions showed that Pho91 supports slower growth and the authors concluded that "A synthetic lethal phenotype was observed when (all) five phosphate transporters were inactivated...". We had cited the same group and the same first author, just using their later study (Wykoff et al., 2007) that had recapitulated the results from PMID11779791 and showed in addition quite good growth of the PHO91 expressing strain on YPD (Suppl. Fig. 2). We had obtained the strains from this group. In reproducing their experiments, we noticed that the growth of Pho91 that these authors had observed is due to incomplete repression of Pho84. They had overexpressed Pho84 from a galactose inducible promotor to generate a background with a regulatable Pi transporter. This trick allowed them to conveniently manipulate the strain and reduce (but not abolish) Pho84 expression by transferring the cells from galactose to glucose for their experiments. Therefore, we chose a more rigorous plasmid shuffling strategy to test the individual P_i transporter, which allows an assessment without the leaky background expression of Pho84 on glucose. In contrast to O'Shea and colleagues, we observed zero growth of a strain expressing only PHO91. We have revised the results section to make this discrepancy more evident and provide a better motivation for our experiment.

(5) It would be nice to see the actual data in Figure 6; not only a quantification. 

We illustrate the phenotype of nuclear Pho4-GFP in panel A. Showing all the images necessary to appreciate the differences between the strains would require including many dozens of images into the figure, which would not be useful.

eLife Assessment

The mechanistic basis for the potential health benefits of NAD⁺ precursors remains incompletely understood. This manuscript provides a useful assessment of the role of SIRT1 in mediating the effects of NMN in mice fed a high-fat diet. The study addresses a key question, though some of the conclusions appear only partially supported by the presented data.

Reviewer #1 (Public review):

Summary:

This manuscript investigates the effects of oral supplementation with nicotinamide mononucleotide (NMN) on metabolism and inflammation in mice with diet-induced obesity, and whether these effects depend on the NAD⁺-dependent enzyme SIRT1. Using control and inducible SIRT1 knockout mice, the authors show that NMN administration mitigates high-fat diet-induced weight gain, enhances energy expenditure, and normalizes fasting glucose and plasma lipid profiles in a largely SIRT1-dependent manner. However, reductions in fat mass and adipose tissue expansion occur independently of SIRT1. Comprehensive plasma proteomic analyses (O-Link and mass spectrometry) reveal that NMN reverses obesity-induced alterations in metabolic and immune pathways, particularly those related to glucose and cholesterol metabolism. Integrative network and causal analyses identify both SIRT1-dependent and -independent protein clusters, as well as potential upstream regulators such as FBXW7, ADIPOR2, and PRDM16. Overall, the study supports that NMN modulates key metabolic and immune pathways through both SIRT1-dependent and alternative mechanisms to alleviate obesity and dyslipidemia in mice.

Strengths:

Well-written manuscript, and state-of-the-art proteomics-based methodologies to assess NMN and SIRT1-dependent effects.

Weaknesses:

Unfortunately, the study design, as well as the data analysis approach taken by the authors, are flawed. This limits the authors' ability to make the proposed conclusions.

Reviewer #2 (Public review):

Summary:

Majeed and colleagues aimed to evaluate whether the metabolic effects of NMN in the context of a high-fat diet are SIRT1 dependent. For this, they used an inducible SIRT1 KO model (SIRT1 iKO), allowing them to bypass the deleterious effects of SIRT1 ablation during development. In line with previous reports, the authors observed that NMN prevents, to some degree, diet-induced metabolic damage in wild-type mice. When doing similar tests on SIRT1 iKO mice, the authors see that some, but not all, of the effects of NMN are abrogated. The phenotypic studies are complemented by plasma proteomic analyses evaluating the influence of the high-fat diet, SIRT1, and NMN on circulating protein profiles.

Strengths:

The mechanistic aspects behind the potential health benefits of NAD+ precursors have been poorly elucidated. This is in part due to the pleiotropic actions of NAD-related molecules on cellular processes. While sirtuins, most notably SIRT1, have been largely hypothesized to be key players in the therapeutic actions of NAD+ boosters, the proof for this in vivo is very limited. In this sense, this work is an important contribution to the field.

Weaknesses:

While the authors use a suitable methodology (SIRT1 iKO mice), the results show very early that the iKO mice themselves have some notable phenotypes, which complicate the picture. The actions of NMN in WT and SIRT1 KO mice are most often presented separately. However, this is not the right approach to evaluate and visualize SIRT1 dependency. Indeed, many of the "SIRT1-dependent" effects of NMN are consequent to the fact that SIRT1 deletion itself has a phenotype equivalent to or larger than that induced by NMN in wild-type mice. This would have been very evident if the two genotypes had been systematically plotted together. Consequently, and despite the value of the study, the results obtained with this model might not allow for solidly established claims of SIRT1 dependency on NMN actions. The fact that some of the effects of SIRT1 deletion are similar to those of NMN supplementation also makes it counterintuitive to propose that activation of SIRT1 is a major driver of NMN actions. Unbiasedly, one might as well conclude that NMN could act by inhibiting SIRT1. The fact that readouts for SIRT1 activity are not explored makes it also difficult to test the influence of NMN on SIRT1 in their experimental setting, or whether compensations could exist.

A second weak point is that the proteomic explorations are interesting, yet feel too descriptive and disconnected from the overall phenotype or from the goal of the manuscript. It would be unreasonable to ask for gain/loss-of-function experiments based on the differentially abundant peptides. Yet, a deeper exploration of whether their altered presence in circulation is consistent with changes in their expression - and, if so, in which tissues - and a clearer discussion on their link to the phenotypes observed would be needed, especially for changes related to SIRT1 and NMN.

Impact on the field and further significance of the work:

Despite the fact that, in my opinion, the authors might not have conclusively achieved their main aim, there are multiple valuable aspects in this manuscript:

(1) It provides independent validation for the potential benefits of NAD+ boosters in the context of diet-induced metabolic complications. Previous efforts using NR or NMN itself have provided contradicting observations. Therefore, additional independent experiments are always valuable to further balance the overall picture.

(2) The metabolic consequences of deleting SIRT1 in adulthood have been poorly explored in previous works. Therefore, irrespective of the actions of NMN, the phenotypes observed are intriguing, and the proteomic differences are also large enough to spur further research to understand the role of SIRT1 as a therapeutic target.

(3) Regardless of the influence of SIRT1, NMN promotes some plasma proteomic changes that are very well worth exploring. In addition, they highlight once more that the in vivo actions of NMN, as those of other NAD+ boosters, are pleiotropic. Hence, this work brings into question whether single gene KO models are really a good approach to explore the mechanisms of action of NAD+ precursors.

Author response:

Reviewer #1 (Public review):

Summary:

This manuscript investigates the effects of oral supplementation with nicotinamide mononucleotide (NMN) on metabolism and inflammation in mice with diet-induced obesity, and whether these effects depend on the NAD⁺-dependent enzyme SIRT1. Using control and inducible SIRT1 knockout mice, the authors show that NMN administration mitigates high-fat diet-induced weight gain, enhances energy expenditure, and normalizes fasting glucose and plasma lipid profiles in a largely SIRT1-dependent manner. However, reductions in fat mass and adipose tissue expansion occur independently of SIRT1. Comprehensive plasma proteomic analyses (O-Link and mass spectrometry) reveal that NMN reverses obesity-induced alterations in metabolic and immune pathways, particularly those related to glucose and cholesterol metabolism. Integrative network and causal analyses identify both SIRT1-dependent and -independent protein clusters, as well as potential upstream regulators such as FBXW7, ADIPOR2, and PRDM16. Overall, the study supports that NMN modulates key metabolic and immune pathways through both SIRT1-dependent and alternative mechanisms to alleviate obesity and dyslipidemia in mice.

Strengths:

Well-written manuscript, and state-of-the-art proteomics-based methodologies to assess NMN and SIRT1-dependent effects.

We thank the reviewer for highlighting that state-of-the-art proteomic research methods used, and we report for the first time on significant changes in plasma proteomics in mice after NMN supplementation in both wild-type and SIRT1-KO mice using a combination of DIA mass spectrometry and Olink.

Weaknesses:

Unfortunately, the study design, as well as the data analysis approach taken by the authors, are flawed. This limits the authors' ability to make the proposed conclusions.

We agree that the administration of tamoxifen, along with the associated weight loss, could affect the obesity phenotype. For this reason, we ensured that both Cre-positive and Cre-negative mice received tamoxifen. Importantly, after the tamoxifen 'washout', the two groups weighed essentially the same. Going forward, we plan to address this comment by performing additional statistical tests on all six experimental groups to gain insights into dependencies. Based on your suggestions, we will clarify the limitations of the study design and improve the data analysis approaches to provide stronger support for our conclusions in the revised version of the paper.

Reviewer #2 (Public review):

Summary:

Majeed and colleagues aimed to evaluate whether the metabolic effects of NMN in the context of a high-fat diet are SIRT1 dependent. For this, they used an inducible SIRT1 KO model (SIRT1 iKO), allowing them to bypass the deleterious effects of SIRT1 ablation during development. In line with previous reports, the authors observed that NMN prevents, to some degree, diet-induced metabolic damage in wild-type mice. When doing similar tests on SIRT1 iKO mice, the authors see that some, but not all, of the effects of NMN are abrogated. The phenotypic studies are complemented by plasma proteomic analyses evaluating the influence of the high-fat diet, SIRT1, and NMN on circulating protein profiles.

Strengths:

The mechanistic aspects behind the potential health benefits of NAD+ precursors have been poorly elucidated. This is in part due to the pleiotropic actions of NAD-related molecules on cellular processes. While sirtuins, most notably SIRT1, have been largely hypothesized to be key players in the therapeutic actions of NAD+ boosters, the proof for this in vivo is very limited. In this sense, this work is an important contribution to the field.

We thank the reviewer for acknowledging the importance of this work to the field. In this report, we provide in vivo evidence of the action of NAD+ boosting, and hope to delineate the action of Sirt1, as well as the pleiotropic effects of NAD-related molecules on cellular and metabolic processes.

Weaknesses:

While the authors use a suitable methodology (SIRT1 iKO mice), the results show very early that the iKO mice themselves have some notable phenotypes, which complicate the picture. The actions of NMN in WT and SIRT1 KO mice are most often presented separately. However, this is not the right approach to evaluate and visualize SIRT1 dependency. Indeed, many of the "SIRT1-dependent" effects of NMN are consequent to the fact that SIRT1 deletion itself has a phenotype equivalent to or larger than that induced by NMN in wild-type mice. This would have been very evident if the two genotypes had been systematically plotted together. Consequently, and despite the value of the study, the results obtained with this model might not allow for solidly established claims of SIRT1 dependency on NMN actions. The fact that some of the effects of SIRT1 deletion are similar to those of NMN supplementation also makes it counterintuitive to propose that activation of SIRT1 is a major driver of NMN actions. Unbiasedly, one might as well conclude that NMN could act by inhibiting SIRT1. The fact that readouts for SIRT1 activity are not explored makes it also difficult to test the influence of NMN on SIRT1 in their experimental setting, or whether compensations could exist.

We thank the reviewer for raising this point and acknowledge the limitations of using Sirt1 iKO mice. However, inducing Sirt1 KO in adulthood is a better alternative than using a homozygous Sirt1 KO mouse model, as the latter leads to embryonic lethality and many other developmental defects (1, 2). The proteomics analysis can provide insight into the effects of SIRT1 deletion under chow and high-fat diet (HFD) conditions, as well as the effects of diet in the presence or absence of nicotinamide mononucleotide (NMN). We will discuss these limitations and present the results for the two genotypes together, as suggested.

A second weak point is that the proteomic explorations are interesting, yet feel too descriptive and disconnected from the overall phenotype or from the goal of the manuscript. It would be unreasonable to ask for gain/loss-of-function experiments based on the differentially abundant peptides. Yet, a deeper exploration of whether their altered presence in circulation is consistent with changes in their expression - and, if so, in which tissues - and a clearer discussion on their link to the phenotypes observed would be needed, especially for changes related to SIRT1 and NMN.

First, we presented the data in this manner as a proof of concept, to demonstrate the effect of the diet on the plasma proteome and corroborate our findings with those published in the literature. We then investigated the effects of NAD boosting and Sirt1 KO in order to identify significant changes. We agree with the reviewer that it would be unreasonable to validate all the differentially abundant proteins. However, we will choose key proteins and assess their expression in different tissues, such as the liver, white adipose tissue (WAT) and muscles, and attempt to connect these changes with the phenotypes.

Impact on the field and further significance of the work:

Despite the fact that, in my opinion, the authors might not have conclusively achieved their main aim, there are multiple valuable aspects in this manuscript:

(1) It provides independent validation for the potential benefits of NAD+ boosters in the context of diet-induced metabolic complications. Previous efforts using NR or NMN itself have provided contradicting observations. Therefore, additional independent experiments are always valuable to further balance the overall picture.

(2) The metabolic consequences of deleting SIRT1 in adulthood have been poorly explored in previous works. Therefore, irrespective of the actions of NMN, the phenotypes observed are intriguing, and the proteomic differences are also large enough to spur further research to understand the role of SIRT1 as a therapeutic target.

(3) Regardless of the influence of SIRT1, NMN promotes some plasma proteomic changes that are very well worth exploring. In addition, they highlight once more that the in vivo actions of NMN, as those of other NAD+ boosters, are pleiotropic. Hence, this work brings into question whether single gene KO models are really a good approach to explore the mechanisms of action of NAD+ precursors.

We thank the reviewer for their analysis in highlighting the valuable aspects of the manuscript and we hope the revised manuscript will further strengthen the key results.

References:

(1) McBurney   MW, Yang   X, Jardine   K, Hixon   M, Boekelheide   K, Webb   JR, Lansdorp   PM, Lemieux   M. The mammalian SIR2alpha protein has a role in embryogenesis and gametogenesis. Mol Cell Biol  2003; 23:38–54.

(2) Cheng   HL, Mostoslavsky   R, Saito   S, Manis   JP, Gu   Y, Patel   P, Bronson   R, Appella   E, Alt   FW, Chua   KF. Developmental defects and p53 hyperacetylation in Sir2 homolog (SIRT1)-deficient mice. Proc Natl Acad Sci U S A  2003; 100:10794–10799.

eLife assessment

The authors identify a novel, conserved link between glycolytic flux and sulfur amino acid metabolism that governs fungal morphological differentiation independently of the cAMP-PKA pathway. This represents an important conceptual advance in understanding metabolic control of development and virulence. While the evidence supporting this connection is compelling, the mechanistic basis of how glycolysis regulates the Met30/Met4 axis requires further experimental clarification.

Reviewer #1 (Public review):

Summary:

Fungal survival and pathogenicity rely on the ability to undergo reversible morphological transitions, which are often linked to nutrient availability. In this study, the authors uncover a conserved connection between glycolytic activity and sulfur amino acid biosynthesis that drives morphogenesis in two fungal model systems. By disentangling this process from canonical cAMP signaling, the authors identify a new metabolic axis that integrates central carbon metabolism with developmental plasticity and virulence.

Strengths:

The study integrates different experimental approaches, including genetic, biochemical, transcriptomic, and morphological analyses, and convincingly demonstrates that perturbations in glycolysis alter sulfur metabolic pathways and thus impact pseudohyphal and hyphal differentiation. Overall, this work offers new and important insights into how metabolic fluxes are intertwined with fungal developmental programs and therefore opens new perspectives to investigate morphological transitioning in fungi.

Weaknesses:

A few aspects could be improved to strengthen the conclusions. Firstly, the striking transcriptomic changes observed upon 2DG treatment should be analyzed in S. cerevisiae adh1 and pfk1 deletion strains, for instance, through qPCR or western blot analyses of sulfur metabolism genes, to confirm that observed changes in 2DG conditions mirror those seen in genetic mutants. Secondly, differences between methionine and cysteine in their ability to rescue the mutant phenotype in both species are not mentioned, nor discussed in more detail. This is especially important as there seem to be differences between S. cerevisiae and C. albicans, which might point to subtle but specific metabolic adaptations.

The authors are also encouraged to refine several figure elements for clarity and comparability (e.g., harmonized axes in bar plots), condense the discussion to emphasize the conceptual advances over a summary of the results, and shorten figure legends.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the interplay between glycolysis and sulfur metabolism in regulating fungal morphogenesis and virulence. Using both Saccharomyces cerevisiae and Candida albicans, the authors demonstrate that glycolytic flux is essential for morphogenesis under nitrogen-limiting conditions, acting independently of the established cAMP-PKA pathway. Transcriptomic and genetic analyses reveal that glycolysis influences the de novo biosynthesis of sulfur-containing amino acids, specifically cysteine and methionine. Notably, supplementation with sulfur sources restores morphogenetic and virulence defects in glycolysis-deficient mutants, thereby linking core carbon metabolism with sulfur assimilation and fungal pathogenicity.

Strengths:

The work identifies a previously uncharacterized link between glycolysis and sulfur metabolism in fungi, bridging metabolic and morphogenetic regulation, which is an important conceptual advance and fungal pathogenicity. Demonstrating that adding cysteine supplementation rescues virulence defects in animal models connects basic metabolism to infection outcomes, which adds to biomedical importance.

Weaknesses:

The proposed model that glycolytic flux modulates Met30 activity post-translationally remains speculative. While data support Met4 stabilization in met30 deletion strains, the mechanism of Met30 modulation by glycolysis is not demonstrated.

Reviewer #3 (Public review):

This study investigates the connection between glycolysis and the biosynthesis of sulfur-containing amino acids in controlling fungal morphogenesis, using Saccharomyces cerevisiae and C. albicans as model organisms. The authors identify a conserved metabolic axis that integrates glycolysis with cysteine/methionine biosynthetic pathways to influence morphological transitions. This work broadens the current understanding of fungal morphogenesis, which has largely focused on gene regulatory networks and cAMP-dependent signaling pathways, by emphasizing the contribution of metabolic control mechanisms. However, despite the novel conceptual framework, the study provides limited mechanistic characterization of how the sulfur metabolism and glycolysis blockade directly drive morphological outcomes. In particular, the rationale for selecting specific gene deletions, such as Met32 (and not Met4), or the Met30 deletion used to probe this pathway, is not clearly explained, making it difficult to assess whether these targets comprehensively represent the metabolic nodes proposed to be critical. Further supportive data and experimental validation would strengthen the claims on connections between glycolysis, sulfur amino acid metabolism, and virulence.

Strengths:

(1) The delineation of how glycolytic flux regulates fungal morphogenesis through a cAMP-independent mechanism is a significant advancement. The coupling of glycolysis with the de novo biosynthesis of sulfur-containing amino acids, a requirement for morphogenesis, introduces a novel and unexpected layer of regulation.

(2) Demonstrating this mechanism in both S. cerevisiae and C. albicans strengthens the argument for its evolutionary conservation and biological importance.

(3) The ability to rescue the morphogenesis defect through exogenous supplementation of sulfur-containing amino acids provides functional validation.

(4) The findings from the murine Pfk1-deficient model underscore the clinical significance of metabolic pathways in fungal infections.

Weaknesses:

(1) While the link between glycolysis and sulfur amino acid biosynthesis is established via transcriptomic and proteomic analysis, the specific regulation connecting these pathways via Met30 remains to be elucidated. For example, what are the expression and protein levels of Met30 in the initial analysis from Figure 2? How specific is this effect on Met30 in anaerobic versus aerobic glycolysis, especially when the pentose phosphate pathway is involved in the growth of the cells when glycolysis is perturbed?

(2) Including detailed metabolite profiling could have strengthened the metabolic connection and provided additional insights into intermediate flux changes, i.e., measuring levels of metabolites to check if cysteine or methionine levels are influenced intracellularly. Also, it is expected to see how Met30 deletion could affect cell growth. Data on Met30 deletion and its effect on growth are not included, especially given that a viable heterozygous Met30 strain has been established. Measuring the cysteine or methionine levels using metabolomic analysis would further strengthen the claims in every section.

(3) In comparison with the previous bioRxiv (doi: https://doi.org/10.1101/2025.05.14.654021) of this article in May 2025 to the recent bioRxiv of this article (doi: https://doi.org/10.1101/2025.05.14.654021), there have been some changes, and Met30 deletion has been recently included, and the chemical perturbation of glycolysis has been added as new data. Although the changes incorporated in the recent version of the article improved the illustration of the hypothesis in Figure 6, which connects glycolysis to Sulfur metabolism, the gene expression and protein levels of all genes involved in the illustrated hypothesis are not consistently shown. For example, in some cases, the Met4 expression is not shown (Figure 4), and the Met30 expression is not shown during profiling (gene expression or protein levels) throughout the manuscript. Lack of consistency in profiling the same set of key genes makes understanding more complicated.

(4) The demonstrated link between glycolysis and sulfur amino acid biosynthesis, along with its implications for virulence in C. albicans, is important for understanding fungal adaptation, as mentioned in the article; however, the Met4 activation was not fully characterized, nor were the data presented when virulence was assessed in Figure 4. Why is Met4 not included in Figure 4D and I? Especially, according to Figure 6, Met4 activation is crucial and guides the differences between glycolysis-active and inactive conditions.

(5) Similarly, the rationale behind selecting Met32 for characterizing sulfur metabolism is unclear. Deletion of Met32 resulted in a significant reduction in pseudohyphal differentiation; why is this attributed only to Met32? What happens if Met4 is deleted? It is not justified why Met32, rather than Met4, was chosen. Figure 6 clearly hypothesizes that Met4 activation is the key to the mechanism.

(6) The comparative RT-qPCR in Figure 5 did not account for sulfur metabolism genes, whereas it was focused only on virulence and hyphal differentiation. Is there data to support the levels of sulfur metabolism genes?

(7) To validate the proposed interlink between sulfur metabolism and virulence, it is recommended that the gene sets (illustrated in Figure 6) be consistently included across all comparative data included throughout the comparisons. Excluding sulfur metabolism genes in Figure 5 prevents the experiment from demonstrating the coordinated role of glycolysis perturbation → sulfur metabolism → virulence. The same is true for other comparisons, where the lack of data on Met30, Met4, etc., makes it hard to connect the hypothesis. It is also recommended to check the gene expression of other genes related to the cAMP pathway and report them to confirm the cAMP-independent mechanism. For example, gap2 deletion was used to confirm the effects of cAMP supplementation, but the expression of this gene was not assessed in the RNA-seq analysis in Figure 2. It would be beneficial to show the expression of cAMP-related genes to completely confirm that they do not play a role in the claims in Figure 2.

(8) Although the NAC supplementation study is included in the new version of the article compared to the previous version in BioRxiv (May 2025), the link to sulfur metabolism is not well characterized in Figure 5 and their related datasets. The main focus of the manuscript is to delineate the role of sulfur metabolism; hence, it is anticipated that Figure 5 will include sulfur-related metabolic genes and their links to pfk1 deletion, using RT-PCR measurements as shown for the virulence genes.

(9) The manuscript would benefit from more information added to the introduction section and literature supports for some of the findings reported earlier, including the role of (i) cAMP-PKA and MAPK pathways, (ii) what is known in the literature that reports about the treatment with 2DG (role of Snf1, HXT1, and HXT3), as well as how gpa2 is involved. Some sentences in the manuscripts are repetitive; it would be beneficial to add more relevant sections to the introduction and discussion to clarify the rationale for gene choices.

eLife Assessment

This valuable work investigates the role of protein N-glycosylation in regulating T-cell activation and function and suggests that B4GALT1 is a potential target for tumor immunotherapy. The strength of evidence is solid, and further mechanistic validation could be provided.

Reviewer #1 (Public review):

Summary:

The study by Yu et al investigated the role of protein N-glycosylation in regulating T-cell activation and functions is an interesting work. By using genome-wide CRISPR/Cas9 screenings, the authors found that B4GALT1 deficiency could activate expression of PD-1 and enhance functions of CD8+ T cells both in vitro and in vivo, suggesting the important roles of protein N-glycosylation in regulating functions of CD8+ T cells, which indicates that B4GALT1 is a potential target for tumor immunotherapy.

Strengths:

The strengths of this study are the findings of novel function of B4GALT1 deficiency in CD8 T cells.

Weaknesses:

However, authors did not directly demonstrate that B4GALT1 deficiency regulates the interaction between TCR and CD8, as well as functional outcomes of this interaction, such as TCR signaling enhancements.

Reviewer #2 (Public review):

Summary:

In this study, the authors identify the N-glycosylation factor B4GALT1 as an important regulator of CD8 T-cell function.

Strengths:

(1) The use of complementary ex vivo and in vivo CRISPR screens is commendable and provides a useful dataset for future studies of CD8 T-cell biology.

(2) The authors perform multiple untargeted analyses (RNAseq, glycoproteomics) to hone their model on how B4GALT1 functions in CD8 T-cell activation.

(3) B4GALT1 is shown to be important in both in vitro T-cell killing assays and a mouse model of tumor control, reinforcing the authors' claims.

Weaknesses:

(1) The authors did not verify the efficiency of knockout in their single-gene KO lines.

(2) As B4GALT1 is a general N-glycosylation factor, the phenotypes the authors observe could formally be attributable to indirect effects on glycosylation of other proteins.

(3) The specific N-glycosylation sites of TCR and CD8 are not identified, and would be helpful for site-specific mutational analysis to further the authors' model.

(4) The study could benefit from further in vivo experiments testing the role of B4GALT1 in other physiological contexts relevant to CD8 T cells, for example, autoimmune disease or infectious disease.

Author response:

Reviewer #1 (Public review):

Summary:

The study by Yu et al investigated the role of protein N-glycosylation in regulating T-cell activation and functions is an interesting work. By using genome-wide CRISPR/Cas9 screenings, the authors found that B4GALT1 deficiency could activate expression of PD-1 and enhance functions of CD8+ T cells both in vitro and in vivo, suggesting the important roles of protein N-glycosylation in regulating functions of CD8+ T cells, which indicates that B4GALT1 is a potential target for tumor immunotherapy.

Strengths:

The strengths of this study are the findings of novel function of B4GALT1 deficiency in CD8 T cells.

Weaknesses:

However, authors did not directly demonstrate that B4GALT1 deficiency regulates the interaction between TCR and CD8, as well as functional outcomes of this interaction, such as TCR signaling enhancements.

We are very sorry that we did not highlight our results in Fig. 5f-h enough. In those figures, we demonstrated the interaction between TCR and CD8 increased significantly in B4GALT1 deficient T-cells, by FRET assays. To confirm the important role of TCR-CD8 interaction in mediating the functions of B4GALT1 in regulating T-cell functions, such as in vitro killing of target cells, we artificially tethered TCR and CD8 by a CD8β-CD3ε fusion protein and tested its functions in both WT and B4GALT1 knockout CD8⁺ T-cell. Our results demonstrate that such fusion protein could bypass the effect of B4GALT1 knockout in CD8⁺T-cells (Fig. 5g-h). Together with the results that B4GALT1 directly regulates the galactosylation of TCR and CD8, those results strongly support the model that B4GALT1 modulates T-cell functions mainly by galactosylations of TCR and CD8 that interfere their interaction.

Reviewer #2 (Public review):

Summary:

In this study, the authors identify the N-glycosylation factor B4GALT1 as an important regulator of CD8 T-cell function.

Strengths:

(1) The use of complementary ex vivo and in vivo CRISPR screens is commendable and provides a useful dataset for future studies of CD8 T-cell biology.

(2) The authors perform multiple untargeted analyses (RNAseq, glycoproteomics) to hone their model on how B4GALT1 functions in CD8 T-cell activation.

(3) B4GALT1 is shown to be important in both in vitro T-cell killing assays and a mouse model of tumor control, reinforcing the authors' claims.

Weaknesses:

(1) The authors did not verify the efficiency of knockout in their single-gene KO lines.

Thank reviewer for reminding. We verified the efficiency of some gRNAs by FACS and Surveyor assay. We will add those data in supplementary results in revised version later.

(2) As B4GALT1 is a general N-glycosylation factor, the phenotypes the authors observe could formally be attributable to indirect effects on glycosylation of other proteins.

please see response to reviewer #1.

(3) The specific N-glycosylation sites of TCR and CD8 are not identified, and would be helpful for site-specific mutational analysis to further the authors' model.

Thank reviewer for suggestion! Unfortunately, there are multiple-sites of TCR and CD8 involved in N-glycosylation (https://glycosmos.org/glycomeatlas). We worry that mutations of all these sites may not only affect glycosylation of TCR and CD8 but also other essential functions of those proteins.

(4) The study could benefit from further in vivo experiments testing the role of B4GALT1 in other physiological contexts relevant to CD8 T cells, for example, autoimmune disease or infectious disease.

Thank reviewer for this great suggestion to expand the roles of B4GALT1 in autoimmune and infection diseases. However, since in current manuscript we are mainly focusing on tumor immunology, we think we should leave these studies for future works.

eLife Assessment

This study presents SegPore, a valuable new method for processing direct RNA nanopore sequencing data, which improves the segmentation of raw signals into individual bases and boosts the accuracy of modified base detection. The evidence presented to benchmark SegPore is solid, and the authors provide a fully documented implementation of the method. SegPore will be of particular interest to researchers studying RNA modifications.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors describe a new computational method (SegPore), which segments the raw signal from nanopore direct RNA-Seq data to improve the identification of RNA modifications. In addition to signal segmentation, SegPore includes a Gaussian Mixture Model approach to differentiate modified and unmodified bases. SegPore uses Nanopolish to define a first segmentation, which is then refined into base and transition blocks. SegPore also includes a modification prediction model that is included in the output. The authors evaluate the segmentation in comparison to Nanopolish and Tombo (RNA002) as well as f5c and Uncalled 4 (RNA004), and they evaluate the impact on m6A RNA modification detection using data with known m6A sites. In comparison to existing methods, SegPore appears to improve the ability to detect m6A, suggesting that this approach could be used to improve the analysis of direct RNA-Seq data.

Strengths:

SegPore address an important problem (signal data segmentation). By refining the signal into transition and base blocks, noise appears to be reduced, leading to improved m6A identification at the site level as well as for single read predictions. The authors provide a fully documented implementation, including a GPU version that reduces run time. The authors provide a detailed methods description, and the approach to refine segments appears to be new.

Reviewer #2 (Public review):

Summary:

The work seeks to improve detection of RNA m6A modifications using Nanopore sequencing through improvements in raw data analysis. These improvements are said to be in the segmentation of the raw data, although the work appears to position the alignment of raw data to the reference sequence and some further processing as part of the segmentation, and result statistics are mostly shown on the 'data-assigned-to-kmer' level.

As such, the title, abstract and introduction stating the improvement of just the 'segmentation' does not seem to match the work the manuscript actually presents, as the wording seems a bit too limited for the work involved.

The work itself shows minor improvements in m6Anet when replacing Nanopolish' eventalign with this new approach, but clear improvements in the distributions of data assigned per kmer. However, these assignments were improved well enough to enable m6A calling from them directly, both at site-level and at read-level.

A large part of the improvements shown appear to stem from the addition of extra, non-base/kmer specific, states in the segmentation/assignment of the raw data, removing a significant portion of what can be considered technical noise for further analysis. Previous methods enforced assignment of (almost) all raw data, forcing a technically optimal alignment that may lead to suboptimal results in downstream processing as datapoints could be assigned to neighbouring kmers instead, while random noise that is assigned to the correct kmer may also lead to errors in modification detection.

For an optimal alignment between the raw signal and the reference sequence, this approach may yield improvements for downstream processing using other tools.

Additionally, the GMM used for calling the m6A modifications provides a useful, simple and understandable logic to explain the reason a modification was called, as opposed to the black models that are nowadays often employed for these types of tasks.

Appraisal:

The authors have shown their methods ability to identify noise in the raw signal and remove their values from the segmentation and alignment, reducing its influences for further analyses. Figures directly comparing the values per kmer do show a visibly improved assignment of raw data per kmer. As a replacement for Nanopolish' eventalign it seems to have a rather limited, but improved effect, on m6Anet results. At the single read level modification modification calling this work does appear to improve upon CHEUI.

Reviewer #3 (Public review):

Summary:

Nucleotide modifications are important regulators of biological function, however, until recently, their study has been limited by the availability of appropriate analytical methods. Oxford Nanopore direct RNA sequencing preserves nucleotide modifications, permitting their study, however many different nucleotide modifications lack an available base-caller to accurately identify them. Furthermore, existing tools are computationally intensive, and their results can be difficult to interpret.

Cheng et al. present SegPore, a method designed to improve the segmentation of direct RNA sequencing data and boost the accuracy of modified base detection.

Strengths:

This method is well described and has been benchmarked against a range of publicly available base callers that have been designed to detect modified nucleotides.

Comment from the Reviewing Editor:

The authors have provided responses to the weaknesses highlighted previously and the reviewers were not asked to comment. The authors have now requested a Version of Record.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors describe a new computational method (SegPore), which segments the raw signal from nanopore direct RNA-Seq data to improve the identification of RNA modifications. In addition to signal segmentation, SegPore includes a Gaussian Mixture Model approach to differentiate modified and unmodified bases. SegPore uses Nanopolish to define a first segmentation, which is then refined into base and transition blocks. SegPore also includes a modification prediction model that is included in the output. The authors evaluate the segmentation in comparison to Nanopolish and Tombo (RNA002) as well as f5c and Uncalled 4 (RNA004), and they evaluate the impact on m6A RNA modification detection using data with known m6A sites. In comparison to existing methods, SegPore appears to improve the ability to detect m6A, suggesting that this approach could be used to improve the analysis of direct RNA-Seq data.

Strengths:

SegPore address an important problem (signal data segmentation). By refining the signal into transition and base blocks, noise appears to be reduced, leading to improved m6A identification at the site level as well as for single read predictions. The authors provide a fully documented implementation, including a GPU version that reduces run time. The authors provide a detailed methods description, and the approach to refine segments appears to be new.

Weaknesses:

The authors show that SegPore reduces noise compared to other methods, however the improvement in accuracy appears to be relatively small for the task of identifying m6A. To run SegPore, the GPU version is essential, which could limit the application of this method in practice.

As discussed in Paragraph 4 of the Discussion, we acknowledge that the improvement of SegPore combined with m6Anet over Nanopolish+m6Anet in bulk in vivo analysis is modest. This outcome is likely influenced by several factors, including alignment inaccuracies caused by pseudogenes or transcript isoforms, the presence of additional RNA modifications that can affect signal baselines, and the fact that m6Anet is specifically trained on Nanopolish-derived events. Additionally, the absence of a modification-free (in vitro transcribed) control sample in the benchmark dataset makes it challenging to establish true k-mer baselines.

Importantly, these challenges do not exist for in vitro data, where the signal is cleaner and better defined. As a result, SegPore achieves a clear and substantial improvement at the single-molecule level, demonstrating the strength of its segmentation approach and its potential to significantly enhance downstream analyses. These results indicate that SegPore is particularly well suited for benchmarking and mechanistic studies of RNA modifications under controlled experimental conditions, and they provide a strong foundation for future developments.

We also recognize that the current requirement for GPU acceleration may limit accessibility in some computational environments. To address this, we plan to further optimize SegPore in future versions to support efficient CPU-only execution, thereby broadening its applicability and impact.

Reviewer #2 (Public review):

Summary:

The work seeks to improve detection of RNA m6A modifications using Nanopore sequencing through improvements in raw data analysis. These improvements are said to be in the segmentation of the raw data, although the work appears to position the alignment of raw data to the reference sequence and some further processing as part of the segmentation, and result statistics are mostly shown on the 'data-assigned-to-kmer' level.

As such, the title, abstract and introduction stating the improvement of just the 'segmentation' does not seem to match the work the manuscript actually presents, as the wording seems a bit too limited for the work involved.

The work itself shows minor improvements in m6Anet when replacing Nanopolish' eventalign with this new approach, but clear improvements in the distributions of data assigned per kmer. However, these assignments were improved well enough to enable m6A calling from them directly, both at site-level and at read-level.

A large part of the improvements shown appear to stem from the addition of extra, non-base/kmer specific, states in the segmentation/assignment of the raw data, removing a significant portion of what can be considered technical noise for further analysis. Previous methods enforced assignment of (almost) all raw data, forcing a technically optimal alignment that may lead to suboptimal results in downstream processing as datapoints could be assigned to neighbouring kmers instead, while random noise that is assigned to the correct kmer may also lead to errors in modification detection.

For an optimal alignment between the raw signal and the reference sequence, this approach may yield improvements for downstream processing using other tools.

Additionally, the GMM used for calling the m6A modifications provides a useful, simple and understandable logic to explain the reason a modification was called, as opposed to the black models that are nowadays often employed for these types of tasks.

Weaknesses:

The manuscript suggests the eventalign results are improved compared to Nanopolish. While this is believably shown to be true (Table 1), the effect on the use case presented, downstream differentiation between modified and unmodified status on a base/kmer, is likely limited for during downstream modification calling the noisy distributions are often 'good enough'. E.g. Nanopolish uses the main segmentation+alignment for a first alignment and follows up with a form of targeted local realignment/HMM test for modification calling (and for training too), decreasing the need for the near-perfect segmentation+alignment this work attempts to provide. Any tool applying a similar strategy probably largely negates the problems this manuscript aims to improve upon. Should a use-case come up where this downstream optimisation is not an option, SegPore might provide the necessary improvements in raw data alignment.

Thank you for this thoughtful comment. We agree that many current state-of-the-art (SOTA) methods perform well on benchmark datasets, but we believe there is still substantial room for improvement. Most existing benchmarks are based on limited datasets, primarily focusing on DRACH motifs in human and mouse transcriptomes. However, m6A modifications can also occur in non-DRACH motifs, where current models tend to underperform. Furthermore, other RNA modifications, such as pseudouridine, inosine, and m5C, remain less studied, and their detection is likely to benefit from more accurate and informative signal modeling.

It is also important to emphasize that raw signal segmentation and RNA modification detection are fundamentally distinct tasks. SegPore focuses on improving the segmentation step by producing a cleaner and more interpretable signal, which provides a stronger foundation for downstream analyses. Even if RNA modification detection algorithms such as m6Anet can partially compensate for noisy segmentation in specific cases, starting from a more accurate signal alignment can still lead to improved accuracy, robustness, and interpretability—particularly in challenging scenarios such as non-canonical motifs or less characterized modifications.

Scientific progress in this field is often incremental, and foundational improvements can have a significant long-term impact. By enhancing raw signal segmentation, SegPore contributes an essential building block that we expect will enable the development of more accurate and generalizable RNA modification detection algorithms as the community integrates it into more advanced workflows.

Appraisal:

The authors have shown their methods ability to identify noise in the raw signal and remove their values from the segmentation and alignment, reducing its influences for further analyses. Figures directly comparing the values per kmer do show a visibly improved assignment of raw data per kmer. As a replacement for Nanopolish' eventalign it seems to have a rather limited, but improved effect, on m6Anet results. At the single read level modification modification calling this work does appear to improve upon CHEUI.

Impact:

With the current developments for Nanopore based modification calling largely focusing on Artificial Intelligence, Neural Networks and the likes, improvements made in interpretable approaches provide an important alternative that enables deeper understanding of the data rather than providing a tool that plainly answers the question of wether a base is modified or not, without further explanation. The work presented is best viewed in context of a workflow where one aims to get an optimal alignment between raw signal data and the reference base sequence for further processing. For example, as presented, as a possible replacement for Nanopolish' eventalign. Here it might enable data exploration and downstream modification calling without the need for local realignments or other approaches that re-consider the distribution of raw data around the target motif, such as a 'local' Hidden Markov Model or Neural Networks. These possibilities are useful for a deeper understanding of the data and further tool development for modification detection works beyond m6A calling.

Reviewer #3 (Public review):

Summary:

Nucleotide modifications are important regulators of biological function, however, until recently, their study has been limited by the availability of appropriate analytical methods. Oxford Nanopore direct RNA sequencing preserves nucleotide modifications, permitting their study, however many different nucleotide modifications lack an available base-caller to accurately identify them. Furthermore, existing tools are computationally intensive, and their results can be difficult to interpret.

Cheng et al. present SegPore, a method designed to improve the segmentation of direct RNA sequencing data and boost the accuracy of modified base detection.

Strengths:

This method is well described and has been benchmarked against a range of publicly available base callers that have been designed to detect modified nucleotides.

Weaknesses:

However, the manuscript has a significant drawback in its current version. The most recent nanopore RNA base callers can distinguish between different ribonucleotide modifications, however, SegPore has not been benchmarked against these models.

The manuscript would be strengthened by benchmarking against the rna004_130bps_hac@v5.1.0 and rna004_130bps_sup@v5.1.0 dorado models, which are reported to detect m5C, m6A_DRACH, inosine_m6A and PseU.

A clear demonstration that SegPore also outperforms the newer RNA base caller models will confirm the utility of this method.

Thank you for highlighting this important limitation. While Dorado, the new ONT basecaller, is publicly available and supports modification-aware basecalling, suitable public datasets for benchmarking m5C, inosine, m6A, and PseU detection on RNA004 are currently lacking. Dorado’s modification-aware models are trained on ONT’s internal data, which is not publicly released. Therefore, it is currently not feasible to directly evaluate or compare SegPore’s performance against Dorado for these RNA modifications.

We would also like to emphasize that SegPore’s primary contribution lies in raw signal segmentation, which is an upstream and foundational step in the RNA modification detection pipeline. As more publicly available datasets for RNA004 modification detection become accessible, we plan to extend our work to benchmark and integrate SegPore with modification detection tasks on RNA004 data in future studies.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Comments based on Author Response

“However, it is valid to compare them on the segmentation task, where SegPore exhibits better performance (Table 1).”

This dodges the point of the actual use case of this approach, as Nanopolish indeed does not support calling modifications for this kind of data, but the general approach it uses might, if adapted for this data, nullify the gains made in the examples presented.

We respectfully disagree with the comment that the advantages demonstrated by SegPore could be “nullified”. Although SegPore’s performance is indeed more modest in in vivo datasets, it shows substantially better performance than CHEUI in in vitro data, clearly demonstrating that improved segmentation directly contributes to more accurate RNA modification estimation.

It is worth noting that CHEUI relies on Nanopolish’s segmentation results for m6A detection. Despite this, SegPore outperforms CHEUI, further supporting the conclusion that segmentation quality has a meaningful impact on downstream modification calling.

In conclusion, based on our current experimental results, SegPore is particularly well suited for RNA modification analysis from in vitro transcribed data, where its improved segmentation provides a clear advantage over existing methods.

Further comments

(2) “(2) Page 3  employ models like Hidden Markov Models (HMM) to segment the signal, but they are prone to noise and inaccuracies”

“That's the alignment/calling part, not the segmentation?”

“Current methods, such as Nanopolish, employ models like Hidden Markov Models (HMM) to segment the signal”

I get the impression the word 'segment' has a different meaning in this work than what I'm used to based on my knowledge around Nanopolish and Tombo, see the deeper code examples further down below.

Additionally, in Nanopolish there is a clear segmentation step (or event detection) without any HMM, then a sort of dynamic timewarping step that aligns the segments and re-combines some segments into a single segment where necessary afterwards. I believe the HMM in Nanopolish is not used at all unless modification calling, but if you can point out otherwise I'm open for proof.

Now I believe it is the meaning of 'segmenting the signal' that confuses me, and now the clarification makes it a bit odd as well:

“Nanopolish and Tombo align the raw signal to the reference sequence to determine which portion of the signal corresponds to each k-mer. We define this process as the segmentation task, referred to as "eventalign" in Nanopolish.”

So now it's clearly stated the raw signal is being 'aligned' and then the process is suddenly defined as the 'segmentation task', and again referred to as "eventalign". Why is it not referred to as the 'alignment task' instead?

I understand the segmentation and alignment parts are closely connected but to me, it seems this work picks the wrong word for the problem being solved.

“Unlike Nanopolish and Tombo, which directly align the raw signal to the reference sequence,…”

Looking at their code, I believe both Nanopolish and Tombo actually do segment the data first (or "event detection"), then they align the segments/events they found, and finally multiple events aligned to the same section are merged. See for yourself:

Nanopolish:

https://github.com/jts/nanopolish/blob/master/src/nanopolish_squiggle_read.cpp<br /> Line 233:

cpp

trim_and_segment_raw(fast5_data.rt, trim_start, trim_end, varseg_chunk, varseg_thresh);

event_table et = detect_events(fast5_data.rt, *ed_params);

Line 270:

cpp

// align events to the basecalled read

std::vector event_alignment = adaptive_banded_simple_event_align(*this, *this->base_model[strand_idx], read_sequence);

Where event detection is further defined at line 268 here:

https://github.com/jts/nanopolish/blob/master/src/thirdparty/scrappie/event_detection.c

Tombo:

https://github.com/nanoporetech/tombo/blob/master/tombo/resquiggle.py

line 1162 and onwards shows a ‘segment_signal’ call and the results are used in a ‘find_adaptive_base_assignment’ call, where ‘segment_signal’ starting at line 1057 tries to find where the signal jumps from a series of similar values to another (start of a base change in the pore), stored in ‘valid_cpts’, and the ‘find_adaptive_base_assignment’ tries to align the resulting segment values to the expected series of values:

python

valid_cpts, norm_signal, new_scale_values = segment_signal(

map_res, num_events, rsqgl_params, outlier_thresh, const_scale)

event_means = ts.compute_base_means(norm_signal, valid_cpts)

dp_res = find_adaptive_base_assignment(

valid_cpts, event_means, rsqgl_params, std_ref, map_res.genome_seq,

start_clip_bases=map_res.start_clip_bases,

seq_samp_type=seq_samp_type, reg_id=map_res.align_info.ID)

These implementations are also why I find the choice of words for what is segmentation and what is alignment a bit confusing in this work, as both Tombo and Nanopolish do a similar, clear segmentation step (or an "event detection" step), followed by the alignment of the segments they determined. The terminology in this work appears to deviate from these.

We thank the reviewer for the detailed comments!

First of all, we sincerely apologize for our earlier misunderstanding regarding how Nanopolish and Tombo operate. Based on a closer examination of their source codes, we now recognize that both tools indeed include a segmentation step based on change-point detection methods, after which the resulting segments are aligned to the reference sequence. We have revised the relevant text in the manuscript accordingly:

- “Current methods, such as Nanopolish, employ change-point detection methods to segment the signal and use dynamic programming methods and HMM to align the derived segments to the reference sequence,”

- “We define this process as the segmentation and alignment task (abbreviated as the segmentation task), which is referred to as “eventalign” in Nanopolish.”

- “In SegPore, we segment the raw signal into small fragments using a Hierarchical Hidden Markov Model (HHMM) and align the mean values of these fragments to the reference, where each fragment corresponds to a sub-state of a k-mer. By contrast, Nanopolish and Tombo use change-point–based methods to segment the signal and employ dynamic programming approaches together with profile HMMs to align the resulting segments to the reference sequence.”

Regarding terminology, we originally borrowed the term “segmentation” from speech processing, where it refers to dividing continuous audio signals into meaningful units. In the context of nanopore signal analysis, segmentation and alignment are often tightly coupled steps. Because of this and because our initial focus was on methodological development rather than terminology, we used the term “segmentation task” to describe the combined process of signal segmentation and alignment.

However, we now recognize that this terminology may cause confusion. Changing every instance of “segmentation” to “segmentation and alignment” or “alignment” would require substantial rewriting of the manuscript. Therefore, in this revision, we have clearly defined “segmentation task” as referring to the combined process of segmentation and alignment. We apologize for any earlier confusion and will adopt the term “alignment” in future work for greater clarity.

(3) I think I do understand the meaning, but I do not understand the relevance of the Aj bit in the last sentence. What is it used for?

Based on the response and another close look at Fig1, it turns out the j refers to extremely small numbers 1 and 2 in step 3. You may want in improve readability for these.

Thank you for the suggestion. We have added subscripts to all nucleotides in the reference sequence in Figure 1A and revised the legend to clarify the notation and improve readability. Specifically, we now include the following explanation:

“For example, A_j denotes the base ‘A’ at the j-th position on the reference sequence. In this example, A₁ and A₂ refer to the first and second occurrences of ‘A’ in the reference sequence, respectively. Accordingly, μ₁ and μ₂ are aligned to A₁, while μ₃ is aligned to A₂”.

(6) “We chose to use the poly(A) tail for normalization because it is sequence-invariant- i.e., all poly(A) tails consist of identical k-mers, unlike transcript sequences which vary in composition. In contrast, using the transcript region for normalization can introduce biases: for instance, reads with more diverse k-mers (having inherently broader signal distributions) would be forced to match the variance of reads with more uniform k-mers, potentially distorting the baseline across k-mers.”

While the next part states there was a benchmark showing SegPore still works without this normalization, I think this answer does not touch upon the underlying issue I'm trying to point out here.

- The biases mentioned here due to a more diverse (or different) subsets of k-mers in a read indeed affects the variance of the signal overall.

- As I pointed out in my earlier remark here, this can be resolved using an approach of 'general normalization', 'mapping to expected signal', 'theil-sen fitting of scale and offset', 're-mapping to expected signal', as Tombo and Nanopolish have implemented.<br /> - Alternatively, one could use the reference sequence (using the read mapping information) and base the expected signal mean and standard deviation on that instead.

- The polyA tail stability as an indicator for the variation in the rest of the signal seems a questionable assumption to me. A 'noisy' pore could introduce a large standard deviation using the polyA tail without increasing the deviations on the signal induced by the variety of k-mers, rather it would be representative for the deviations measured within a single k-mer segment. I thought this possible discrepancy is to be expected from a worn out pore, hence I'd imagine reads sequenced later in a run to provide worse results using this method.

In the current version it is not the statement that is unclear, it is the underlying assumption of how this works that I question.

We thank the reviewer for raising this important point and for the insightful discussion. Our choice of using the poly(A) tail for normalization is based on the working hypothesis that the poly(A) signal reflects overall pore-level variability and provides a stable reference for signal scaling. We find this to be a practical and effective approach in most experimental settings.

We agree that more sophisticated strategies, such as “general normalization” or iterative fitting to the expected signal (as implemented in Tombo and Nanopolish), could in principle generate a "better" normalization. However, these approaches are significantly more challenging to implement in practice. This is because signal normalization and alignment are mutually dependent processes: baseline estimates for k-mers influence alignment accuracy, while alignment accuracy, in turn, affects baseline calculation. This interdependence becomes even more complex in the presence of RNA modifications, which alter signal distributions and further confound model fitting.

It is worth noting that this limitation is already evident in our results. As shown in Figure 4B (first and second k-mers), Nanopolish produces more dispersed baselines than SegPore, even for these unmodified k-mers, suggesting inherent limitations in its normalization strategy. Ideally, baselines for the same k-mer should remain highly consistent across different reads.

In contrast, poly(A)-based normalization offers a simpler and more robust solution that avoids this circular dependency. Because poly(A) sequences are compositionally homogeneous, they enable reliable estimation of scaling parameters without assumptions about k-mer composition or modification state. Regarding the reviewer’s concern about pore instability, we mitigate this issue by including only high-quality, confidently mapped reads in our analysis, which reduces the likelihood of incorporating signals from degraded or “noisy” pores.

We fully agree that exploring more advanced normalization strategies is an important direction for future work, and we plan to investigate such approaches as the field progresses.

(8) “In the remainder of this paper, we refer to these resulting events as the output of eventalign analysis or the segmentation task.”

Picking only one descriptor rather than two alternatives would be easier to follow (and I'd prefer the first).

Thank you for the suggestion. We have revised the sentence to:

“In the remainder of this paper, we refer to these resulting events as the output of eventalign analysis, which also represents the final output of the segmentation and alignment task.”

(9) “Additionally, a complete explanation of how the weighted mean is computed is provided in Section 5.3 of Supplementary Note 1. It is derived from signal points that are assigned to a given 5mer.”

I believe there's no more mention of a weighted mean, and I don't get any hits when searching for 'weight'. Is that intentional?

We apologize for the misplacement of the formulas. We have updated Section 5.3 of Supplementary Note 1 to clarify the definition of the weighted mean. Because multiple current signal segments may be aligned to a single k-mer, we computed the weighted mean for each k-mer across these segments, where the weight corresponds to the number of data points assigned to “curr” state in each event.

(17) Response: We revised the sentence to clarify the selection criteria: "For selected 5mers “that exhibit both a clearly unmodified and a clearly” “modified signal component”, “SegPore reports the modification rate at each site,” “as well as the modification state of that site on individual reads.””

So is this the same set described on page 13 ln 343 or not?

“Due to the differences between human (Supplementary Fig. S2A) and mouse (Supplementary Fig. S2B), only six 5mers were found to have m6A annotations in the test data's ground truth (Supplementary Fig. S2C). For a genomic location to be identified as a true m6A modification site, it had to correspond to one of these six common 5mers and have a read coverage of greater than 20.”

I struggle to interpret the 'For selected 5mers' part, as I'm not sure if this is a selection I'm supposed to already know at this point in the text or if it's a set just introduced here. If the latter, removing the word 'selected' would clear it up for me.

We apologize for the confusion. What we mean is that when pooling signals aligned to the same k-mer across different genomic locations and reads, only a subset of k-mers exhibit a bimodal distribution — one peak corresponding to the unmodified state and another to the modified state. Other k-mers show a unimodal distribution, making it impossible to reliably estimate modification levels. We refer to the subset of k-mers that display a bimodal distribution as the “selected” k-mers.

The “selected k-mers” described on page 13, line 343, must additionally have ground truth labels available in both the training and test datasets. There are 10 k-mers with ground truth annotations in the training data and 11 in the test data, and only 6 of these k-mers are shared between the two datasets, therefore only those 6 overlapping k-mers are retained for evaluation. These 6 k-mers satisfy both criteria: (1) exhibiting a bimodal distribution and (2) having ground truth annotations in both training and test sets.

To improve clarity, we have removed the term “selected” from the sentence.

(21) "Tombo used the "resquiggle" method to segment the raw signals, and we standardized the segments using the “poly(A)” tail to ensure a fair comparison “(See” “preprocessing section in Materials and Methods)."”

In the Materials and Methods:

“The raw signal segment corresponding to the poly(A) tail is used to standardize the raw signal for each read.”

I cannot find more detailed information here on what the standardization does, do you mean to refer to Supplementary Note 1, Section 3 perhaps?

Thank you for pointing this out. Yes, the standardization procedure is described in detail in Supplementary Note 1, Section 3. Tombo itself does not segment and align the raw signal on the absolute pA scale, which can result in very large variance in the derived events if the raw signal is used directly. To ensure a fair comparison, we therefore applied the same preprocessing steps to Tombo’s raw signals as we did for SegPore, using only the event boundary information from Tombo while standardizing the signal in the same way.

We have revised the sentence for clarity as follows:

“Tombo used the "resquiggle" method to segment the raw signals, but the resulting signals are not reported on the absolute pA scale. To ensure a fair comparison with SegPore, we standardized the segments using the poly(A) tail in the same way as SegPore (See preprocessing section in Materials and Methods).”

(22A) The table shown does help showing the benchmark is unlikely to be 'cheated'. However I am suprised to see the Avg std for Nanopolish and Tombo going up instead of down, as I'd expect the transition values to increase the std, and hence, removing them should decrease these values. So why does this table show the opposite?

I believe this table is not in the main text or the supplement, would it not be a good idea to cover this point somewhere in the work?

Thank you for this insightful comment. In response, we carefully re-examined our analysis and identified a bug in the code related to boundary removal for Nanopolish. We have now corrected this issue and included the updated results in Supplementary Table S1 of the revised manuscript. As shown in the updated table, the average standard deviations decrease after removing the boundary regions for both Nanopolish and Tombo.

We have now included this table in Supplementary Table S1 in the revised manuscript and added the following clarification:

“It is worth noting that the data points corresponding to the transition state between two consecutive 5-mers are not included in the calculation of the standard deviation in SegPore’s results in Table 1. However, their exclusion does not affect the overall conclusion, as there are on average only ~6 points per 5-mer in the transition state (see Supplementary Table S1 for more details).”

(22B) As mentioned in 2), I'm happy there's a clear definition of what is meant but I found the chosen word a bit odd.

We apologize for the earlier unclear terminology. We now refer to it as the segmentation and alignment task, abbreviated as the segmentation task.

(23) Reading back I can gather that from the text earlier, but the summation of what is being tested is this:

“including Tombo, MINES (31), Nanom6A (32), m6Anet, Epinano (33), and CHEUI (20). “

next, the identifier "Nanopolish+m6Anet" is, aside from the figure itself, only mentioned in the discussion. Adding a line that explains that "Nanopolish+m6Anet" is the default method of running m6Anet and "SegPore+m6Anet" replaces the Nanopolish part for m6Anet with Segpore, rather than jumping straight to "SegPore+m6Anet", would clarify where this identifier came from.

Thank you for the helpful suggestion. We have added the identifier to the revised manuscript as follows:

“Given their comparable methodologies and input data requirements, we benchmarked SegPore against several baseline tools, including Tombo, MINES (31), Nanom6A (32), m6Anet, Epinano (33), and CHEUI (20). By default, MINES and Nanom6A use eventalign results generated by Tombo, while m6Anet, Epinano, and CHEUI rely on eventalign results produced by Nanopolish. In Fig. 3C, ‘Nanopolish+m6Anet’ refers to the default m6Anet pipeline, whereas ‘SegPore+m6Anet’ denotes a configuration in which Nanopolish’s eventalign results are replaced with those from SegPore.”

(24) For completeness I'd expect tickmarks and values on the y-axis as well.

Thank you for the suggestion. We have updated Figures 3A and 3B in the revised manuscript to include tick marks and values on the y-axis as requested.

(25) Considering this statement and looking back at figure 3a and 3b, wouldn't this be easier to observe if the histograms/KDE's were plotted with overlap in a single figure?

We appreciate the suggestion. However, we believe that overlaying Figures 3A and 3B into a single panel would make the visualization cluttered and more difficult to interpret.

(29) Please change the sentence in the text to make that clear. As it is written now (while it's the same number of motifs, so one might guess it) it does not seem to refer to that particular set of motifs and could be a new selection of 6 motifs.

We appreciate the suggestion and have revised the sentence for clarity as follows:

“We evaluated m6A predictions using two approaches: (1) SegPore’s segmentation results were fed into m6Anet, referred to as SegPore+m6Anet, which works for all DRACH motifs and (2) direct m6A predictions from SegPore’s Gaussian Mixture Model (GMM), which is limited to the six selected 5-mers shown in Supplementary Fig. S2C that exhibit clearly separable modified and unmodified components in the GMM (see Materials and Methods for details). ”

(31) I think we have a different interpretation of the word 'leverage', or perhaps what it applies to. I'd say it leverages the jiggling if there's new information drawn from the jiggling behaviour. It's taking it into account if it filters for it. The HHMM as far as I understand tries to identify the jiggles, and ignore their values for the segmentation etc. So while one might see this as an approach that "leverages the hypothesis", I don't see how this HHMM "leverages the jiggling property" itself.

Thank you for the helpful suggestion. We have replaced the word “leverages” with “models” in the revised manuscript.

New points

pg6ln166: “…we extract the aligned raw signal segment and reference sequence segment from Nanopolish's events [...] we extract the raw signal segment corresponding to the transcript region for each input read based on Nanopolish's poly(A) detection results.”

It is not clear as to why this different approach is applied for these two cases in this part of the text.

Thank you for pointing this out. The two approaches refer to different preprocessing strategies for in vivo and in vitro data.

For in vivo data, a large proportion of reads do not span the full-length transcript and often map only to a portion of the reference sequence. Moreover, because a single gene can generate multiple transcript isoforms, a read may align equally well to several possible transcripts. Therefore, we extract only the raw signal segment that corresponds to the mapped portion of the transcript for each read.

In contrast, for in vitro data, the transcript sequence is known precisely. As a result, we can directly extract all raw signals following the poly(A) tail and align them to the complete reference sequence.

pg10ln259: An important distinction from classical global alignment algorithms is that one or multiple base blocks may align with a single 5mer.”

If there was usually a 1:1 mapping the alignment algorithm would be more or less a direct match, so I think the multiple blocks aligning to a 5mer thing is actually quite common.

Thank you for the comment. The “classical global alignment algorithm” here refers to the Needleman–Wunsch algorithm used for sequence alignment. Our intention was to highlight the conceptual difference between traditional sequence alignment and nanopore signal alignment. In classical sequence alignment, each base typically aligns to a single position in the reference. In contrast, in nanopore signal alignment, one or multiple signal segments — corresponding to varying dwell times of the motor protein — can align to a single 5-mer.

We have revised the sentence as follows:

“An important distinction from classical global alignment algorithms (Needleman–Wunsch algorithm)……”

pg13ln356: "dwell time" is not defined or used before, I guess it's effectively the number of raw samples per segment but this should be clarified.

Thank you for pointing this out. We have now added a clear definition of dwell time in the text as follows:

"such as the normalized mean μ_i, standard deviation σ_i, dwell time l_i (number of data points in the event)."

pg13ln358: “Feature vectors from 80% of the genomic locations were used for training, while the remaining 20% were set aside for validation.”

I assume these are selected randomly but this is not explicitly stated here and should be.

Yes, they are randomly selected. We have revised the sentence as follows:

“Feature vectors from a randomly selected 80% of the genomic locations were used for training, while the remaining 20% were set aside for validation.”

pg18ln488: The manuscript now evaluates RNA004 and compares against f5c and Uncalled4. It mentions the differences between RNA004 and RNA002, namely kmer size and current levels, but does not explain where the starting reference model values for the RNA004 model come from: In pg18ln492 they state "RNA004 provides reference values for 9mers", then later they seem to use a 5mer parameter table (pg19ln508), are they re-using the same table from RNA002 or did they create a 5mer table from the 9mer reference table?

We apologize for the confusion. The reference model table for RNA004 9-mers is obtained from f5c (the array named ‘rna004_130bps_u_to_t_rna_9mer_template_model_builtin_data’in  https://raw.githubusercontent.com/hasindu2008/f5c/refs/heads/master/src/model.h).

Author response image 1.

We have revised the subsection header “5-mer parameter table” in the Method to “5-mer & 9-mer parameter table” to highlight this and added a paragraph about how to obtain the 9-mer parameter table:

“In the RNA004 data analysis (Table 2), we obtained the 9-mer parameter table from the source code of f5c (version 1.5). Specifically, we used the array named ‘rna004_130bps_u_to_t_rna_9mer_template_model_builtin_data’ from the following file: https://raw.githubusercontent.com/hasindu2008/f5c/refs/heads/master/src/model.h (accessed on 17 October 2025).”

Also, in page 18 line 195, we added the following sentence:

“The 9-mer parameter table in pA scale for RNA004 data provided by f5c (see Materials and Methods) was used in the analysis.”

pg19ln520: “Additionally, due to the differences of the k-mer motifs between human and mouse (Supplementary Fig. S2), six shared 5mers were selected to demonstrate SegPore's performance in modification prediction directly.”

"the differences" - in occurrence rates, as I gather from the supplementary figure, but it would be good to explicitly state it in this sentence itself too.

Thank you for the helpful suggestion. We agree that the original sentence was vague. The main reason for selecting only six 5-mers is the difference in the availability of ground truth labels for specific k-mer motifs between human and mouse datasets. We have revised the sentence accordingly:

“Additionally, due to the differences in the availability of ground truth labels for specific k-mer motifs between human and mouse (Supplementary Fig. S2), six shared 5-mers were selected to directly demonstrate SegPore’s performance in modification prediction.”

pg24ln654: “SegPore codes current intensity levels”

"codes" is meant to be "stores" I guess? Perhaps "encodes"?

Thank you for the suggestion. We have now replaced it with “encodes” in the revised manuscript.

Lastly, looking at the feedback from the other reviewers comment:

The 'HMM' mentioned in line 184 looks fine to me, the HHMM is 2 HMM's in a hierarchical setup and the text now refers to one of these HMM layers. If this is to be changed it would need to state the layer (e.g. "the outer HHMM layer") throughout the text instead.

We agree with this assessment and believe that the term “inner HMM” is accurate in this context, as it correctly refers to one of the two HMM layers within the HHMM structure. Therefore, we have decided to retain the current terminology.

Reviewer #3 (Recommendations for the authors):

I recommend the publication of this manuscript, provided that the following comments are addressed.

Page 5, Preprocessing: You comment that the poly(A) tail provides a stable reference that is crucial for the normalisation of all reads. How would this step handle reads that have interrupted poly(A) tails (e.g. in the case of mRNA vaccines that employ a linker sequence)? Or cell types that express TENT4A/B, which can include transcripts with non-A residues in the poly(A) tail: https://www.science.org/doi/full/10.1126/science.aam5794.

It depends on Nanopolish’s ability to reliably detect the poly(A) tail. In general, the poly(A) region produces a long stretch of signals fluctuating around a current level of ~108.9 pA (RNA002) with relatively stable variation, which allows it to be identified and used for normalization.

For in vivo data, if the poly(A) tail is interrupted (e.g., due to non-A residues or linker sequences), two scenarios are possible:

(1) The poly(A) tail may not be reliably detected, in which case the corresponding read will be excluded from our analysis.

(2) Alternatively, Nanopolish may still recognize the initial uninterrupted portion of the poly(A) signal, which is typically sufficient in length and stability to be used for signal normalization.

For in vitro data, the poly(A) tails are uninterrupted, so this issue does not arise.

All analyses presented in this study are based exclusively on reads with reliably detected poly(A) tails.

Page 7, 5mer parameter table: r9.4_180mv_70bps_5mer_RNA is an older kmer model (>2 years). How does your method perform with the newer RNA kmer models that do permit the detection of multiple ribonucleotide modifications? Addressing this comment would be beneficial, however I understand that it would require the generation of new data, as limited RNA004 datasets are available in the public domain.

“r9.4_180mv_70bps_5mer_RNA” is the most widely used k-mer model for RNA002 data. Regarding the newer k-mer models, we believe the reviewer is referring to the “modification basecalling” models available in Dorado, which are specifically designed for RNA004 data. At present, SegPore can perform RNA modification estimation only on RNA002 data, as this is the platform for which suitable training data and ground truth annotations are available. Evaluating SegPore’s performance with the newer RNA004 modification models would require new datasets containing known modification sites generated with RNA004 chemistry. Since such data are currently unavailable, we have not yet been able to assess SegPore under these conditions. This represents an important future direction for extending and validating our method.

The Methods and Results sections contain redundant information -please streamline the information in these sections and reduce the redundancy.

We thank the reviewer for this suggestion and acknowledge that there is some overlap between the Methods and Results sections. However, we feel that removing these parts could compromise the clarity and readability of the manuscript, especially given that Reviewer 2 emphasized the need for clearer explanations. We therefore decided to retain certain methodological descriptions in the Results section to ensure that key steps are understandable without requiring the reader to constantly cross-reference the Methods.

Minor comments

Please be consistent when referring to k-mers and 5-mers (sometimes denoted as 5mers - please change to 5-mers throughout).

We have revised the manuscript to ensure consistency and now use “5-mers” throughout the text.

Introduction

Lines 80 - 112: Please condense this section to roughly half the length (1-2 paragraphs). In general, the results described in the introduction should be very brief, as they are described in full in the results section.

Thank you for the suggestion. We have condensed the original three paragraphs into a single, more concise paragraph as follows:

"SegPore is a novel tool for direct RNA sequencing (DRS) signal segmentation and alignment, designed to overcome key limitations of existing approaches. By explicitly modeling motor protein dynamics during RNA translocation with a Hierarchical Hidden Markov Model (HHMM), SegPore segments the raw signal into small, biologically meaningful fragments, each corresponding to a k-mer sub-state, which substantially reduces noise and improves segmentation accuracy. After segmentation, these fragments are aligned to the reference sequence and concatenated into larger events, analogous to Nanopolish’s “eventalign” output, which serve as the foundation for downstream analyses. Moreover, the “eventalign” results produced by SegPore enhance interpretability in RNA modification estimation. While deep learning–based tools such as m6Anet classify RNA modifications using complex, non-transparent features (see Supplementary Fig. S5), SegPore employs a simple Gaussian Mixture Model (GMM) to distinguish modified from unmodified nucleotides based on baseline current levels. This transparent modeling approach improves confidence in the predictions and makes SegPore particularly well-suited for biological applications where interpretability is essential."

Line 104: Please change "normal adenosine" to "adenosine".

We have revised the manuscript as requested and replaced all instances of “normal adenosine” with “adenosine” throughout the text.

Materials and Methods

Line 176: Please reword "...we standardize the raw current signals across reads, ensuring that the mean and standard deviation of the poly(A) tail are consistent across all reads." To "...we standardize the raw current signals for each read, ensuring that the mean and standard deviation are consistent across the poly(A) tail region."

We have changed sentence as requested.

“Since the poly(A) tail provides a stable reference, we standardize the raw current signals for each read, ensuring that the mean and standard deviation are consistent across the poly(A) tail region.”

Line 182: Please describe the RNA translocation hypothesis, as this is the first mention of it in the text. Also, why is the Hierachical Hidden Markov model perfect for addressing the RNA translocation hypothesis? Explain more about how the HHMM works and why it is a suitable choice.

We have revised the sentence as requested:

“The RNA translocation hypothesis (see details in the first section of Results) naturally leads to the use of a hierarchical Hidden Markov Model (HHMM) to segment the raw current signal.”

The motivation of the HHMM is explained in detail in the the first section “RNA translocation hypothesis” of Results. As illustrated in Figure 2, the sequencing data suggest that RNA molecules may translocate back and forth (often referred to as jiggling) while passing through the nanopore. This behavior results in complex current fluctuations that are challenging to model with a simple HMM. The HHMM provides a natural framework to address this because it can model signal dynamics at two levels. The outer HMM distinguishes between two major states — base states (where the signal corresponds to a stable sub-state of a k-mer) and transition states (representing transitions from one base state to the next). Within each base state, an inner HMM models finer signal variation using three states — “curr”, “prev”, and “next” — corresponding to the current k-mer sub-states and its neighboring k-mer sub-states. This hierarchical structure captures both the stable signal patterns and the stochastic translocation behavior, enabling more accurate and biologically meaningful segmentation of the raw current signal.

Line 184: do you mean HHMM? Please be consistent throughout the text.

As explained in the previous response, the HHMM consists of two layers: an outer HMM and an inner HMM. The term “HMM” in line 184 is meant to be read together with “inner” at the end of line 183, forming the phrase “inner HMM.” It seems the reviewer may have overlooked this when reading the text.

Line 203: please delete: "It is obviously seen that".

We have removed the phrase “It is obviously seen that” from the sentence as requested. The revised sentence now reads:

“The first part of Eq. 2 represents the emission probabilities, and the second part represents the transition probabilities.”

Line 314, GMM for 5mer parameter table re-estimation: "Typically, the process is repeated three to five times until the5mer parameter table stabilizes." How is the stabilisation of the 5mer parameter table quantified? What is a reasonable cut-off that would demonstrate adequate stabilisation of the 5mer parameter table? Please add details of this to the text.

We have revised the sentence to clarify the stabilization criterion as follows:

“Typically, the process is repeated three to five times until the 5-mer parameter table stabilizes (when the average change of mean values of all 5-mers is less than 5e-3).”

Results

Line 377: Please edit to read "Traditional base calling algorithms such as Guppy and Albacore assume that the RNA molecule is translocated unidirectionally through the pore by the motor protein."

We have revised the sentence as:

“In traditional basecalling algorithms such as Guppy and Albacore, we implicitly assume that the RNA molecule is translocated through the pore by the motor protein in a monotonic fashion, i.e., the RNA is pulled through the pore unidirectionally.”

Line 555, m6A identification at the site level: "For six selected m6A motifs, SegPore achieved an ROC AUC of 82.7% and a PR AUC of 38.7%, earning the third best performance compared with deep leaning methods m6Anet and CHEUI (Fig. 3D)." So SegPore performs third best of all deep learning methods. Do you recommend its use in conjunction with m6Anet for m6A detection? Please clarify in the text. This will help to guide users to possible best practice uses of your software.

Thank you for the suggestion. We have added a clarification in the revised manuscript to guide users.

“For practical applications, we recommend taking the intersection of m6A sites predicted by SegPore and m6Anet to obtain high-confidence modification sites, while still benefiting from the interpretability provided by SegPore’s predictions.”

Figures.

Figure 1A please refer to poly(A) tail, rather than polyA tail.

We have updated it to poly(A) tail in the revised manuscript.

eLife Assessment

This valuable study provides insights into the role of Pten mutations in SHH-medulloblastoma, by using mouse models to resolve the effects of heterozygous vs homozygous mutations on proliferation and cell death throughout tumorigenesis. The experiments presented are convincing, with rigorous quantifications and orthogonal experimentation provided throughout, and the models employing sporadic oncogene induction, rather than EGL-wide genetic modifications, represent an advancement in experimental design. However, the study remains limited, such that the biological conclusions do not extend greatly from those in the extant literature. This could be addressed with additional experimentation focused on cell cycle kinetic changes at early stages, as well as greater characterization of macrophage phenotypes (e.g., microglia vs circulating monocytes). The work will be of interest to medical biologists studying general cancer mechanisms, as the function of Pten may be similar across tumor types.

Reviewer #1 (Public review):

Summary:

This paper investigates how Pten loss influences the development of medulloblastoma using mouse models of Shh-driven MB. Previous studies have shown that Pten heterozygosity can accelerate tumorigenesis in models where the entire GNP compartment has MB-promoting mutations, raising questions about how Pten levels and context interact, especially when cancer-causing mutations are more sporadic. Here, the authors create an allelic series combining sporadic, cell-autonomous induction of SmoM2 with Pten loss in granule neuron progenitors. In their models, Pten heterozygosity does not significantly impact tumor development, whereas complete Pten loss accelerates tumour onset. Notably, Pten-deficient tumours accumulate differentiated cells, reduced cell death, and decreased macrophage infiltration. At early stages, before tumour establishment, they observe EGL hyperplasia and more pre-tumour cells in S phase, leading them to suggest that Pten loss initially drives proliferation but later shifts towards differentiation and accumulation of death-resistant, postmitotic cells. Overall, this is a well-executed and technically elegant study that confirms and extends earlier findings with more refined models. The phenotyping is strong, but the mechanistic insight is limited, especially with respect to dosage effects and macrophage biology.

Strengths:

The work is carefully executed, and the models-using sporadic oncogene induction rather than EGL-wide genetic manipulations-represent an advance in experimental design. The deeper phenotyping, including single-cell RNA-seq and target validation, adds rigor.

Weaknesses:

The biological conclusions largely confirm findings from previous studies (Castellino et al, 2010; Metcalf et al, 2013), showing that germline or conditional Pten heterozygosity accelerates tumorigenesis, generates tumors with a very similar phenotype, including abundant postmitotic cells, and reduced cell death.

The second stated goal - to understand why Pten dosage might matter - remains underdeveloped. The difference between earlier models using EGL-wide SmoA1 or Ptch loss versus sporadic cell-autonomous SmoM2 induction and Pten loss in this study could reflect model-specific effects or non-cell-autonomous contributions from Pten-deficient neighbouring cells in the EGL, for example. However, the study does not explore these possibilities. For instance, examining germline Pten loss in the sporadic SmoM2 context could have provided insight into whether dosage effects are cell-autonomous or dependent on the context.

The observations on macrophages are intriguing but preliminary. The reduction in Iba1+ cells could reflect changes in microglia, barrier-associated macrophages, or infiltrating peripheral macrophages, but these populations are not distinguished. Moreover, the functional relevance of these immune changes for tumor initiation or progression remains unexplored.

Reviewer #2 (Public review):

The authors sought to answer several questions about the role of the tumor suppressor PTEN in SHH-medulloblastoma formation. Namely, whether Pten loss increases metastasis, understanding why Pten loss accelerates tumor growth, and the effect of single-copy vs double-copy loss on tumorigenesis. Using an elegant mouse model, the authors found that Pten mutations do not increase metastasis in a SmoD2-driven SHH-medulloblastoma mouse model, based on extensive characterization of the presence of spinal cord metastases. Upon examining the cellular phenotype of Pten-null tumors in the cerebellum, the authors made the interesting and puzzling observation that Pten loss increased the differentiation state of the tumor, with fewer cycling cells, seemingly in contrast to the higher penetrance and decreased latency of tumor growth.

The authors then examined the rate of cell death in the tumor. Interestingly, Pten-null tumors had fewer dying cells, as assessed by TUNEL. In addition, the tumors expressed differentiation markers NeuN and SyP, which are rare in SHH-MB mouse models. This reduction in dying cells is also evident at earlier stages of tumor growth. By looking shortly after Pten-loss induction, the authors found that Pten loss had an immediate impact on increasing the proliferative state of GCPs, followed by enhancing the survival of differentiated cells. These two pro-tumor features together account for the increased penetrance and decreased latency of the model. While heterozygous loss of Pten also promoted proliferation, it did not protect against cell death.

Interestingly, loss of Pten alone in GCPs caused an increase in cerebellar size throughout development. The authors suggest that Pten normally constrains GCP proliferation, although they did not check whether reduced cell death is also contributing to cerebellum size.

Lastly, the authors examined macrophage infiltration and found that there was less macrophage infiltration in the Pten-null tumors. Using scRNA-seq, they suggest that the observed reduction in macrophages might be due to an immunosuppressive tumor microenvironment.

This mouse model will be of high relevance to the medulloblastoma community, as current models do not reflect the heterogeneity of the disease. In addition, the elegant experimentation into Pten function may be relevant to cancer biologists outside of the medulloblastoma field.

Strengths:

The in-depth characterisation of the mouse model is a major strength of the study, including multiple time points and quantifications. The single-cell sequencing adds a nice molecular feature, and this dataset may be relevant to other researchers with specific questions of Pten function.

Weaknesses:

One weakness of the study was the examination of the macrophage phenotype, which did not include quantification (only single images), so it is difficult to assess whether this reduction of macrophages holds true across multiple samples. Future studies will also be needed to assess whether Pten-mutated patient medulloblastomas also have a differentiation phenotype, but this is difficult to assess given the low number of samples worldwide.

eLife Assessment

Pinho et al use in vivo calcium imaging and chemogenetic approaches to examine the involvement of hippocampal sub-regions across the different stages of a sensory preconditioning task in mice. They find evidence for sensory preconditioning in male mice. They also find that, in these mice, CaMKII-positive neurons in the dorsal hippocampus encode the audio-visual association that forms in stage 1 of the task. The evidence in support of these findings is convincing. The important study will be of interest to researchers in the fields of learning and memory and/or hippocampus function.

Reviewer #1 (Public review):

Summary:

The study by Pinho et al. presents a novel behavioral paradigm for investigating higher-order conditioning in mice. The authors developed a task that creates associations between light and tone sensory cues, driving mediated learning. They observed sex differences in task acquisition, with females demonstrating faster mediated learning compared to males. Using fiber photometry and chemogenetic tools, the study reveals that the dorsal hippocampus (dHPC) plays a central role in encoding mediated learning. These findings are crucial for understanding how environmental cues, which are not directly linked to positive/negative outcomes, contribute to associative learning. Overall, the study is well-designed, with robust results, and the experimental approach aligns with the study's objectives.

Strengths:

The authors develop a robust behavioral paradigm to examine higher-order associative learning in mice.

They discover a sex-specific component influencing mediated learning.

Using fiber photometry and chemogenetic techniques, the authors identify the dorsal hippocampus but not the ventral hippocampus, plays a crucial for encoding mediated learning.

Reviewer #2 (Public review):

Pinho et al. developed a new auditory-visual sensory preconditioning procedure in mice. They observed sex differences in this task, with male, but not female mice acquiring preconditioned fear. Using photometry, they observed activation of the dorsal and ventral hippocampus during sensory preconditioning (tone + light) and direct conditioning (light + shock). Finally, the authors combined their sensory preconditioning task with DREADDs. They found that inhibition of CamKII-positive cells in the dorsal hippocampus, but not the ventral hippocampus, during the preconditioning phase impaired the formation of sensory preconditioned fear. However, inhibiting the same cells during phase two (light + shock) had no effect.

Strengths:

(1) The authors develop a robust auditory-visual sensory preconditioning protocol in male mice. Research on the neurobiology of sensory preconditioning has primarily used rats as subjects. The development of a mouse protocol will be very beneficial to the field, allowing researchers to take advantage of the many transgenic mouse lines.

(2) They find sex differences in the acquisition of sensory preconditioning, raising the importance of adapting behavioral procedures to sex

(3) They identify the dorsal (but not ventral) hippocampus as a key region for the integration of sensory information during the preconditioning phase, furthering our understanding of the role of the hippocampus in integrating experience.

Comments on the revisions:

Thank you for addressing my concerns in considerable detail. I have no more suggestions for the authors.

Reviewer #3 (Public review):

Summary:

Pinho et al., investigated the role of the dorsal VS ventral hippocampus and gender differences in mediated learning. While previous studies already established the engagement of the hippocampus in sensory preconditioning, the authors here took advantages of freely-moving fiber photometry recording and chemogenetics to observe and manipulate sub-regions of the hippocampus (drosal VS ventral) in a cell-specific manner. Importantly, the authors validated the sensory preconditioning procedure in male mice. The authors found no evidence of sensory preconditioning in female mice, but rather a generalization effect, stressing the importance of gender differences in fear learning. After validation of a sensory preconditioning procedure in male mice using light and tone neutral stimuli and a mild foot shock as the unconditioned stimulus, the authors used fiber photometry to record from all neurons VS parvalbumin_positive_only neurons in the dorsal hippocampus or ventral hippocampus of male mice during both preconditioning and conditioning phases. They found an increased activity of all neurons, PV+_only neurons, and CAMKII+ neurons in both sub-regions of the hippocampus during both preconditioning and conditioning phases. Finally, the authors found that chemogenetic inhibition of CaMKII+ neurons (but not PV+_only neurons) in the dorsal (but not ventral) hippocampus specifically prevented the formation of an association between the two neutral stimuli (i.e., light and tone cues). This manipulation had no effect on the direct association between the light cue and the mild foot shock. This set of data (1) validates sensory preconditioning in male mice, and stresses the importance of taking gender effect into account; (2) validates the recruitment of dorsal and ventral hippocampi during preconditioning and conditioning phases; (3) and further establishes the specific role of CaMKII+ neurons in the dorsal hippocampus, but not ventral hippocampus, in the formation of an association between two neutral stimuli, but not between a neutral-stimulus and a mild foot shock.

Strengths:

The authors developed a sensory preconditioning procedure in male mice to investigate mediated learning using light and tone cues as neutral stimuli, and a mild foot shock as the unconditioned stimulus. They provide evidence of a gender effect in the formation of light-cue association. The authors took advantage of fiber-photometry and chemogenetics to target sub-regions of the hippocampus, in a cell-specific manner and investigate their role during different phases of a sensory conditioning procedure, and developed a DeepLabCut-based strategy to assess freezing fear responses.

Weaknesses:

The authors went further than previous studies by investigating the role of sub-regions the hippocampus in mediated learning, however, there are a few weaknesses that should be addressed in future studies:

(1) This study found a generalization effect in female mice only. While the authors attempted to neutralize this effect, the mechanism underlying this gender effect and whether female mice can display evidence for mediated learning has yet to be determined.

(2) One of the main effects from which derives the conclusion of this study (i.e., deficit of mediated learning in male mice when CAMKII+ neurons are inhibited in the dorsal HPC during the preconditioning phase) lies in the absence of a significant difference of the freezing response before and during the tone cue presentation when CAMKII+ are chemogenetically inhibited during the Probe Test Tone phase (cf. Fig. 4 Panel B, DPCd group). The fear response before the tone cue presentation in this group (DPCd) seems higher than in Controls_d and DPTd groups and could have masked a mediated learning effect.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review): 

Summary: 

The study by Pinho et al. presents a novel behavioral paradigm for investigating higher-order conditioning in mice. The authors developed a task that creates associations between light and tone sensory cues, driving mediated learning. They observed sex differences in task acquisition, with females demonstrating faster-mediated learning compared to males. Using fiber photometry and chemogenetic tools, the study reveals that the dorsal hippocampus (dHPC) plays a central role in encoding mediated learning. These findings are crucial for understanding how environmental cues, which are not directly linked to positive/negative outcomes, contribute to associative learning. Overall, the study is well-designed, with robust results, and the experimental approach aligns with the study's objectives. 

Strengths: 

(1) The authors develop a robust behavioral paradigm to examine higher-order associative learning in mice. 

(2) They discover a sex-specific component influencing mediated learning, with females exhibiting enhanced learning abilities. 

(3) Using fiber photometry and chemogenetic techniques, the authors identify the dorsal hippocampus but not the ventral hippocampus, which plays a crucial for encoding mediated learning.

We appreciate the strengths highlighted by the Reviewer and the valuable and complete summary of our work.

Weaknesses: 

(1) The study would be strengthened by further elaboration on the rationale for investigating specific cell types within the hippocampus.  

We thank the Reviewer for highlighting this important point. In the revised manuscript, we have added new information (Page 11, Lines 27-34) to specifically explain the rational of studying the possible cell-type specific involvement in sensory preconditioning.

(2) The analysis of photometry data could be improved by distinguishing between early and late responses, as well as enhancing the overall presentation of the data.  

According to the Reviewer comment, we have included new panels in Figure 3E and the whole Supplementary Figure 4, which separates the photometry data across different preconditioning and conditioning sessions, respectively. Overall, this data suggests that there are no major changes on cell activity in both hippocampal regions during the different sessions as similar light-tone-induced enhancement of activity is observed. These findings have been incorporated in the Results Section (Page 12, Lines 13-15, 19-20 and 35-36).

(3) The manuscript would benefit from revisions to improve clarity and readability.

Based on the fair comment, we have gone through the text to increase clarity and readability.

Reviewer #2 (Public review): 

Summary: 

Pinho et al. developed a new auditory-visual sensory preconditioning procedure in mice and examined the contribution of the dorsal and ventral hippocampus to learning in this task. Using photometry they observed activation of the dorsal and ventral hippocampus during sensory preconditioning and conditioning. Finally, the authors combined their sensory preconditioning task with DREADDs to examine the effect of inhibiting specific cell populations (CaMKII and PV) in the DH on the formation and retrieval/expression of mediated learning. 

Strengths: 

The authors provide one of the first demonstrations of auditory-visual sensory preconditioning in male mice. Research on the neurobiology of sensory preconditioning has primarily used rats as subjects. The development of a robust protocol in mice will be beneficial to the field, allowing researchers to take advantage of the many transgenic mouse lines. Indeed, in this study, the authors take advantage of a PV-Cre mouse line to examine the role of hippocampal PV cells in sensory preconditioning. 

We acknowledge the Reviewer´s effort and for highlighting the strengths of our work.

Weaknesses: 

(1) The authors report that sensory preconditioning was observed in both male and female mice. However, their data only supports sensory preconditioning in male mice. In female mice, both paired and unpaired presentations of the light and tone in stage 1 led to increased freezing to the tone at test. In this case, fear to the tone could be attributed to factors other than sensory preconditioning, for example, generalization of fear between the auditory and visual stimulus.

We thank the comment raised by the Reviewer. At first, we were hypothesizing that female mice were somehow able to associate light and tone although they were presented separately during the preconditioning sessions. Thus, we designed new experiments (shown in Supplementary Figure 2D) to test if we would observe data congruent with our initial hypothesis or with fear generalization as proposed by the reviewer. We have performed a new experiment comparing a Paired group with two additional control groups that are (i) an Unpaired group where we increased the time between the light and tone presentations and (ii) an experimental group where the light was absent during the conditioning. Clearly, the new results indicate the presence of fear generalization in female mice aswe found a significant cue-induced increase on freezing responses in all the experimental groups tested. In accordance with the Reviewer’s suggestion, we can conclude that mediated learning is not correctly observed in female mice using the protocol described (i.e. with 2 conditioning sessions). All these new results forced us to reorganize the structure and the figures of the manuscript to focus more in male mice in the Main Figures whereas showing the data with female mice in Supplementary Figures. Overall, our data clearly revealed the necessity to have adapted behavioral protocols for each sex demonstrating sex differences in sensory preconditioning, which was added in the Discussion Section (Page 15, lines 12-37).

(2) In the photometry experiment, the authors report an increase in neural activity in the hippocampus during both phase 1 (sensory preconditioning) and phase 2 (conditioning). In the subsequent experiment, they inhibit neural activity in the DH during phase 1 (sensory preconditioning) and the probe test, but do not include inhibition during phase 2 (conditioning). It was not clear why they didn't carry forward investigating the role of the hippocampus during phase 2 conditioning. Sensory preconditioning could occur due to the integration of the tone and shock during phase two, or retrieval and chaining of the tonelight-shock memories at test. These two possibilities cannot be differentiated based on the data. Given that we do not know at which stage the mediate learning is occurring, it would have been beneficial to additionally include inhibition of the DH during phase 2. 

Following the Reviewer’s valuable comment, we have conducted a new experiment where we have chemogenetically inhibited the CaMKII-positive neurons of the dHPC during the conditioning to explore their involvement in mediated learning formation. Notably, the inhibition of principal neurons of the dHPC during conditioning does not impair the formation ofthe mediated learning in our hands. These new results are now shown in Supplementary Figure 7G and added in the Results section (Page 13, Lines 19-23).

(3) In the final experiment, the authors report that inhibition of the dorsal hippocampus during the sensory preconditioning phase blocked mediated learning. While this may be the case, the failure to observe sensory preconditioning at test appears to be due more to an increase in baseline freezing (during the stimulus off period), rather than a decrease in freezing to the conditioned stimulus. Given the small effect, this study would benefit from an experiment validating that administration of J60 inhibited DH cells. Further, given that the authors did not observe any effect of DREADD inhibition in PV cells, it would also be important to validate successful cellular silencing in this protocol.  

According to the Reviewer comments, we have performed new experiments to validate the use of J60 to inhibit hippocampal cells that are shown in Supplementary Figure 7 E-F for CaMKII-positive neurons, in which J60 administration tends to decrease the frequency of calcium events both in the dHPC and vHPC. Furthermore, in Supplementary Figure 8 B-C we show that J60 is also able to modify calcium events in PV-positive interneurons. Although,the best method to validate the use of DREADD (i.e. to inhibit hippocampal cell activity) could be electrophysiology recordings, we lack this technique in our laboratory. Thus, in order to adress the reviewer comment, we decided to combine the DREADD modulation through J60 administration with photometry recordings, where several tendencies are confirmed. In addition, a similar approach has been used in another preprint of the lab (https://doi.org/10.1101/2025.08.29.673009), where there is an increase of phospho-PDH, a marker of neuronal inhibition upon J60 administration in the dHPC, as well as in other experiments conducted from a collaborator lab where they were able to observe a modulation of SOM-positive interneurons activity upon J60 administration (PhD defense of Miguel Sabariego, University Pompeu Fabra, Barcelona). 

Reviewer #3 (Public review): 

Summary: 

Pinho et al. investigated the role of the dorsal vs ventral hippocampus and the gender differences in mediated learning. While previous studies already established the engagement of the hippocampus in sensory preconditioning, the authors here took advantage of freely-moving fiber photometry recording and chemogenetics to observe and manipulate sub-regions of the hippocampus (dorsal vs. ventral) in a cell-specific manner. The authors first found sex differences in the preconditioning phase of a sensory preconditioning procedure, where males required more preconditioning training than females for mediating learning to manifest, and where females displayed evidence of mediated learning even when neutral stimuli were never presented together within the session. 

After validation of a sensory preconditioning procedure in mice using light and tone neutral stimuli and a mild foot shock as the unconditioned stimulus, the authors used fiber photometry to record from all neurons vs. parvalbumin_positive_only neurons in the dorsal hippocampus or ventral hippocampus of male mice during both preconditioning and conditioning phases. They found increased activity of all neurons, as well as PV+_only neurons in both sub-regions of the hippocampus during both preconditioning and conditioning phases. Finally, the authors found that chemogenetic inhibition of CaMKII+ neurons in the dorsal, but not ventral, hippocampus specifically prevented the formation of an association between the two neutral stimuli (i.e., light and tone cues), but not the direct association between the light cue and the mild foot shock. This set of data: (1) validates the mediated learning in mice using a sensory preconditioning protocol, and stresses the importance of taking sex effect into account; (2) validates the recruitment of dorsal and ventral hippocampi during preconditioning and conditioning phases; and (3) further establishes the specific role of CaMKII+ neurons in the dorsal but not ventral hippocampus in the formation of an association between two neutral stimuli, but not between a neutralstimulus and a mild foot shock. 

Strengths: 

The authors developed a sensory preconditioning procedure in mice to investigate mediated learning using light and tone cues as neutral stimuli, and a mild foot shock as the unconditioned stimulus. They provide evidence of a sex effect in the formation of light-cue association. The authors took advantage of fiber-photometry and chemogenetics to target sub-regions of the hippocampus, in a cell-specific manner and investigate their role during different phases of a sensory conditioning procedure. 

We thank the Reviewer for the extensive summary of our work and for giving interesting value to some of our findings.

Weaknesses: 

The authors went further than previous studies by investigating the role of sub-regions of the hippocampus in mediated learning, however, there are several weaknesses that should be noted: 

(1) This work first validates mediated learning in a sensory preconditioning procedure using light and tone cues as neutral stimuli and a mild foot shock as the unconditioned stimulus, in both males and females. They found interesting sex differences at the behavioral level, but then only focused on male mice when recording and manipulating the hippocampus. The authors do not address sex differences at the neural level. 

We appreciate the comment of the Reviewer. Indeed, thanks to other Reviewer comments during this revision process (see Point 1 of Reviewer #2), we performed an additional experiment that reveals that using the described protocol in female mice we observed fear generalization rather than mediated learning responding. This data pointed to the need of sex-specific changes in the behavioral protocols to measure sensory preconditioning. The revised version of the manuscript, although highlighting these sex differences in behavioral performance (see Supplementary Figure 2), is more focused in male mice and, accordingly, all photometry or chemogenetic experiments are performed using male mice. In future studies, once we are certain to have a sensory preconditioning paradigm working in female mice, it will be very interesting to study if the same hippocampal mechanisms mediating this behavior in male mice are also observed in female mice.  

(2) As expected in fear conditioning, the range of inter-individual differences is quite high. Mice that didn't develop a strong light-->shock association, as evidenced by a lower percentage of freezing during the Probe Test Light phase, should manifest a low percentage of freezing during the Probe Test Tone phase. It would interesting to test for a correlation between the level of freezing during mediated vs test phases. 

Thanks to the comment raised by the reviewer, we generated a new set of data correlating mediated and direct fear responses. As it can be observed in Supplementary Figure 3, there is a significant correlation between mediated and direct learning in male mice (i.e. the individuals that freeze more in the direct learning test, correlate with the individuals that express more fear response in the mediated learning test). In contrast, this correlation is absent in female mice, further confirming what we have explained above. We have highlighted this new analysis in the Results section (Page 11, Lines 20-24).

(3) The use of a synapsin promoter to transfect neurons in a non-specific manner does not bring much information. The authors applied a more specific approach to target PV+ neurons only, and it would have been more informative to keep with this cell-specific approach, for example by looking also at somatostatin+ inter-neurons. 

The idea behind using a pan neuronal promoter was to assess in general terms how neuronal activity in the hippocampus is engaged during different phases of the lighttone sensory preconditioning. However, the comment of the Reviewer is very pertinent and, as suggested, we have generated some new data targeting CaMKII-positive neurons (see Point 4 below). Finally, although it could be extremely interesting, we believe that targeting different interneuron subtypes is out of the scope of the present work. However, we have added this in the Discussion Section as a future perspective/limitation of our study (Page 17, Lines 9-24).   

(4) The authors observed event-related Ca2+ transients on hippocampal pan-neurons and PV+ inter-neurons using fiber photometry. They then used chemogenetics to inhibit CaMKII+ hippocampal neurons, which does not logically follow. It does not undermine the main finding of CaMKII+ neurons of the dorsal, but not ventral, hippocampus being involved in the preconditioning, but not conditioning, phase. However, observing CaMKII+ neurons (using fiber photometry) in mice running the same task would be more informative, as it would indicate when these neurons are recruited during different phases of sensory preconditioning. Applying then optogenetics to cancel the observed event-related transients (e.g., during the presentation of light and tone cues, or during the foot shock presentation) would be more appropriate.  

We have generated new photometry data to analyze the activity of CaMKII-positive neurons during the preconditioning phase to confirm their engagement during the light-tone pairings. Thus, we infused a CaMKII-GCAMP calcium sensor into the dHPC and vHPC of mice and we recorded its activity during the 6 preconditioning sessions. The new results can be found in Figure 3 and explained in the Results section (Page 12, Lines 26-36). The results clearly show an engagement of CaMKII-positive neurons during the light-tone pairing observed both in the dHPC and vHPC. Finally, although the suggestion of performing optogenetic manipulations would be very elegant, we expect to have convinced the reviewer that our chemogenetic results clearly show and are enough to demonstrate the involvement of dHPC in the formation of mediated learning in the Light-Tone sensory preconditioning paradigm. However, we have added this in the Discussion Section as a future perspective/limitation of our study (Page 17, Lines 9-24).  

(5) Probe tests always start with the "Probe Test Tone", followed by the "Probe Test Light". "Probe Test Tone" consists of an extinction session, which could affect the freezing response during "Probe Test Light" (e.g., Polack et al. (http://dx.doi.org/10.3758/s13420-013-0119-5)). Preferably, adding a group of mice with a Probe Test Light with no Probe Test Tone could help clarify this potential issue. The authors should at least discuss the possibility that the tone extinction session prior to the "Probe Test Light" could have affected the freezing response to the light cue. 

We appreciate the comment raised by the reviewer. However, we think that our direct learning responses are quite robust in all of our experiments and, thus, the impact of a possible extinction based on the tone presentation should not affect our direct learning. However, as it is an important point, we have discussed it in the Discussion Section (Page 17, Lines 12-14).  

Reviewer #4 (Public review): 

Summary 

Pinho et al use in vivo calcium imaging and chemogenetic approaches to examine the involvement of hippocampal sub-regions across the different stages of a sensory preconditioning task in mice. They find clear evidence for sensory preconditioning in male but not female mice. They also find that, in the male mice, CaMKII-positive neurons in the dorsal hippocampus: (1) encode the audio-visual association that forms in stage 1 of the task, and (2) retrieve/express sensory preconditioned fear to the auditory stimulus at test. These findings are supported by evidence that ranges from incomplete to convincing. They will be valuable to researchers in the field of learning and memory. 

We appreciate the summary of our work and all the constructive comments raised by the Reviewer, which have greatly improved the clarity and quality of our manuscript.  

Abstract 

Please note that sensory preconditioning doesn't require the stage 1 stimuli to be presented repeatedly or simultaneously. 

The reviewer is right, and we have corrected and changed that information in the revised abstract.  

"Finally, we combined our sensory preconditioning task with chemogenetic approaches to assess the role of these two hippocampal subregions in mediated learning."  This implies some form of inhibition of hippocampal neurons in stage 2 of the protocol, as this is the only stage of the protocol that permits one to make statements about mediated learning. However, it is clear from what follows that the authors interrogate the involvement of hippocampal sub-regions in stages 1 and 3 of the protocol - not stage 2. As such, most statements about mediated learning throughout the paper are potentially misleading (see below for a further elaboration of this point). If the authors persist in using the term mediated learning to describe the response to a sensory preconditioned stimulus, they should clarify what they mean by mediated learning at some point in the introduction. Alternatively, they might consider using a different phrase such as "sensory preconditioned responding". 

Considering the arguments of the Reviewer, we have modified our text in the Abstract and through the main text. Moreover, based on a comment of Reviewer #2 (Point 2) we have generated new data demonstrating that dHPC does not seem to be involved in mediated learning formation during Stage 2, as its inhibition does not impair sensory preconditioning responding. This new data can be seen in Supplementary Figure 7G.  

Introduction 

"Low-salience" is used to describe stimuli such as tone, light, or odour that do not typically elicit responses that are of interest to experimenters. However, a tone, light, or odour can be very salient even though they don't elicit these particular responses. As such, it would be worth redescribing the "low-salience" stimuli in some other terms. 

Through the revised version of the manuscript, we have replaced the term “lowsalience” by “innocuous stimuli” or avoiding any adjective as we think is not necessary.  

"These higher-order conditioning processes, also known as mediated learning, can be captured in laboratory settings through sensory preconditioning procedures2,6-11."  Higher-order conditioning and mediated learning are not interchangeable terms: e.g., some forms of second-order conditioning are not due to mediated learning. More generally, the use of mediated learning is not necessary for the story that the authors develop in the paper and could be replaced for accuracy and clarity. E.g., "These higher-order conditioning processes can be studied in the laboratory using sensory preconditioning procedures2,6-11." 

According to the Reviewer proposal, we have modified the text. 

In reference to Experiment 2, it is stated that: "However, when light and tone were separated on time (Unpaired group), male mice were not able to exhibit mediated learning response (Figure 2B) whereas their response to the light (direct learning) was not affected (Figure 2D). On the other hand, female mice still present a lower but significant mediated learning response (Figure 2C) and normal direct learning (Figure 2E). Finally, in the No-Shock group, both male (Figure 2B and 2D) and female mice (Figure 2C and 2E) did not present either mediated or direct learning, which also confirmed that the exposure to the tone or light during Probe Tests do not elicit any behavioral change by themselves as the presence of the electric footshock is required to obtain a reliable mediated and direct learning responses."  The absence of a difference between the paired and unpaired female mice should not be described as "significant mediated learning" in the latter. It should be taken to indicate that performance in the females is due to generalization between the tone and light. That is, there is no sensory preconditioning in the female mice. The description of performance in the No-shock group really shouldn't be in terms of mediated or direct learning: that is, this group is another control for assessing the presence of sensory preconditioning in the group of interest. As a control, there is no potential for them to exhibit sensory preconditioning, so their performance should not be described in a way that suggests this potential. 

All these comments are very pertinent and also raised by Reviewer #2 (Point 1, see above). In the revised version of the manuscript, we have carefully changed, when necessary, our interpretation of the results (e.g. in the case of the No-Shock group). In addition, we have generated new data that confirm that using similar conditions (i.e. 2 conditioning sessions in our SPC) in female mice we observe fear generalization and not a confident sensory preconditioning responding. In our opinion, this is not discarding the presence of mediated learning in female mice but suggesting that adapted protocols must be used in each sex. These results forced us to change the organization of the Figures but we hope the reviewer would agree with all the changes proposed. In addition, we have re-wrote a paragraph in the Discussion Section to explain these sex differences (see Page 15, lines 12-37). 

Methods - Behavior 

I appreciate the reasons for testing the animals in a new context. This does, however, raise other issues that complicate the interpretation of any hippocampal engagement: e.g., exposure to a novel context may engage the hippocampus for exploration/encoding of its features - hence, it is engaged for retrieving/expressing sensory preconditioned fear to the tone. This should be noted somewhere in the paper given that one of its aims is to shed light on the broader functioning of the hippocampus in associative processes. 

This general issue - that the conditions of testing were such as to force engagement of the hippocampus - is amplified by two further features of testing with the tone. The first is the presence of background noise in the training context and its absence in the test context. The second is the fact that the tone was presented for 30 s in stage 1 and then continuously for 180s at test. Both changes could have contributed to the engagement of the hippocampus as they introduce the potential for discrimination between the tone that was trained and tested. 

We have now added these pertinent comments in a “Study limitations” paragraph found in the Discussion Section (Page 17, Lines 9-24). Indeed, the different changes of context (including the presence of background noise) have been implemented by the fact that during the setting up of the paradigm we had problems of fear generalization (also in male mice). Similarly, differences in cue exposure between the preconditioning phase and the test phase were also decided based on important differences between previous protocols used in rats compared to how mice are responding. Certainly, mice were not able to adapt their behavioral responses when shorter time windows exposing the cue were used as it clearly happens with rats [1].

Results - Behavior 

The suggestion of sex differences based on differences in the parameters needed to generate sensory preconditioning is interesting. Perhaps it could be supported through some set of formal analyses. That is, the data in supplementary materials may well show that the parameters needed to generate sensory preconditioning in males and females are not the same. However, there needs to be some form of statistical comparison to support this point. As part of this comparison, it would be neat if the authors included body weight as a covariate to determine whether any interactions with sex are moderated by body weight.  

Regarding the comparison between male and female mice, although the comments of the Reviewer are pertinent and interesting, we think that with the new data generated is not appropriate to compare both sexes as we still have to optimize the SPC protocol for female mice. 

What is the value of the data shown in Figure 1 given that there are no controls for unpaired presentations of the sound and light? In the absence of these controls, the experiment cannot have shown that "Female and male mice show mediated learning using an auditory-visual sensory preconditioning task" as implied by its title. Minimally, this experiment should be relabelled. 

Based on the new data generated with female mice, we have decided to remove Figure 1 and re-organize the structure of the manuscript. We hope that the Reviewer would agree that this has improved the clarity of the manuscript.  

"Altogether, this data confirmed that we successfully set up an LTSPC protocol in mice and that this behavioral paradigm can be used to further study the brain circuits involved in higherorder     conditioning."  Please insert the qualifier that LTSPC was successfully established in male mice. There is no evidence of LTSPC in female mice. 

We fully agree with the Reviewer and our new findings further confirm this issue. Thus, we have changed the statement in the revised version of the manuscript.  

Results - Brain 

"Notably, the inhibition of CaMKII-positive neurons in the dHPC (i.e. J60 administration in DREADD-Gi mice) during preconditioning (Figure 4B), but not before the Probe Test 1 (Figure 4B), fully blocked mediated, but not direct learning (Figure  4D)." The right panel of Figure 4B indicates no difference between the controls and Group DPC in the percent change in freezing from OFF to ON periods of the tone. How does this fit with the claim that CaMKII-positive neurons in the dorsal hippocampus regulate associative formation during the session of tone-light exposures in stage 1 of sensory preconditioning? 

To improve the quality of the figures and to avoid possible redundancies between panels, in the new version of the manuscript, we have decided to remove all the panels regarding the percentage of change. However, in our opinion regarding the issue raised by the Reviewer, the inhibition of the dHPC clearly induced an impairment of mediated learning as animals do not change their behavior (i.e. there is no significant increase of freezing between OFF and ON periods) when the tone appears in comparison with the other two groups. The graphs indicating the percentage of change (old version of the manuscript) was a different manner to show the presence of tone- or light-induced responses in each experimental group. Thus, a significant effect (shown by # symbol) meant that in that specific experimental group there was a significant change in behavior (freezing) when the cue (tone or light) appeared compared when there was no cue (OFF period). Thus, in the old panel 4B commented by the Reviewer, in our opinion, the absence of significance in the group where the dHPC has been inhibited during thepreconditioning, compared to the other groups, where a clear significant effect can be observed, indicate an impairment of mediated learning formation. However, to avoid any confusion, we have slightly modified the text to strictly mention what is being analyzed and/or shown in the graphs and, as mentioned, the graphs of percentage of change have been removed.  

Discussion 

"When low salience stimuli were presented separated on time or when the electric footshock was absent, mediated and direct learning were abolished in male mice. In female mice, although light and tone were presented separately during the preconditioning phase, mediated learning was reduced but still present, which implies that female mice are still able to associate the two low-salience stimuli." 

This doesn't quite follow from the results. The failure of the female unpaired mice to withhold their freezing to the tone should not be taken to indicate the formation of a light-tone association across the very long interval that was interpolated between these stimulus presentations. It could and should be taken to indicate that, in female mice, freezing conditioned to the light simply generalized to the tone (i.e., these mice could not discriminate well between the tone and light). 

As discussed above, we fully agree with the Reviewer and all the manuscript has been modified as described above. 

"Indeed, our data suggests that when hippocampal activity is modulated by the specific manipulation of hippocampal subregions, this brain region is not involved during retrieval."  Does this relate to the results that are shown in the right panel of Figure 4B, where there is no significant difference between the different groups? If so, how does it fit with the results shown in the left panel of this figure, where differences between the groups are observed? 

"In line with this, the inhibition of CaMKII-positive neurons from the dorsal hippocampus, which has been shown to project to the restrosplenial cortex56, blocked the formation of mediated learning." 

Is this a reference to the findings shown in Figure 4B and, if so, which of the panels exactly? That is, one panel appears to support the claim made here while the other doesn't. In general, what should the reader make of data showing the percent change in freezing from stimulus OFF to stimulus ON periods? 

In our opinion, as pointed above, the graphs indicating the percentage of change were a different manner to show the presence of tone- or light-induced behavioral responses in each experimental group. Thus, a significant effect (shown by # symbol) meant that in this specific experimental group there was a significant change in behavior (freezing) when the cue (tone or light appear) compared when there was no cue (OFF period). Thus, in the old panel 4B commented by the Reviewer, in our opinion, the absence of significance in the group where the dHPC has been inhibited during the preconditioning, compared to the other groups where a clear significant effect can be observed, indicates an impairment of mediated learning formation. In the revised version of the manuscript, we have rephrased these sentences to stick to what the graphs are showing and, as explained, the graphs of percentage of change have been removed.

Reviewer #1 (Recommendations for the authors): 

The authors may address the following questions: 

(1) The study identifies major sex differences in the conditioning phase, with females showing faster learning. Since hormonal fluctuations can influence learning and behavior, it would be helpful for the authors to comment on whether they tracked the estrous cycle of the females and whether any potential effects of the cycle on mediated learning were considered. 

This is a relevant and important point raised by the Reviewer. In our study we did not track the estrous cycle to investigate whether it exists any effect of the cycle on mediated learning, which could be an interesting project by itself. Although in the revised version of the manuscript we provide new information regarding the mediated learning performance in male and female mice, we agree with the reviewer that sex hormones may account for the observed sex differences. However, the aim of the present work was to explore potential sex differences in mediated learning responding rather than to investigate the specific mechanisms behind these potential sex differences. 

For this reason and to avoid adding further complexity to our present study, we did not check the estrous cycle in the female mice, the testosterone levels in male mice or analyze the amount of sex hormones during different phases of the sensory preconditioning task. Indeed, we think that checking the estrous cycle in female mice would still not be enough to ascertain the role of sex hormones because checking the androgen levels in male mice would also be required. In line with this, meta-analysis of neuroscience literature using the mouse model as research subjects [2-4]  has revealed that data collected from female mice (regardless of the estrous cycle) did not vary more than the data from males. In conclusion, we think that using randomized and mixed cohorts of male and female mice (as in the present study) would provide the same degree of variability in both sexes. Nevertheless, we have added a sentence to point to this possibility in the Discussion Section (Page 15, lines 32-37). 

(2) The rationale for including parvalbumin (PV) cells in the study could be clarified. Is there prior evidence suggesting that this specific cell type is involved in mediated learning? This could apply to sensory stimuli not used in the current study.

In the revised version of the manuscript, we have better clarified why we targeted PV interneurons, specifically mentioning previous studies [5] (see Page 11, Lines 27-34). 

(3) The photometry recordings from the dHPC during the preconditioning phase, shown in Figure 3, are presented as average responses. It would be beneficial to separate the early vs. late trials to examine whether there is an increase in hippocampal activity as the associative learning progresses, rather than reporting the averaged data. Additionally, to clarify the dynamics of the dHPC in associative learning, the authors could compare the magnitude of photometry responses when light and tone stimuli are presented individually in separate sessions versus when they are presented closely in time to facilitate associative learning.

As commented above, according to the Reviewer’s comment, we have now included a new Supplementary Figure 4, which splits the photometry data by the different preconditioning and conditioning sessions. Overall, this data suggests that there are no major changes on cell activity in both hippocampal regions during the different sessions as similar light-tone-induced enhancement of activity is observed. There is only an interesting trend in the activity of Pan-Neurons over the onset of light during conditioning sessions. All this is included now in the Results Section (Page 12, Line 13-15).

(4) The authors note that PV cell responses recorded with GCaMP were similar to general hippocampal neurons, yet chemogenetic manipulations of PV cells did not impact behavior. A more detailed discussion of this discrepancy would be helpful. 

As suggested by the Reviewer, we have included additional Discussion to explain the potential discrepancy between the activity of PV interneurons assessed by photometry and its modulation by chemogenetics (see Page 16, Lines 27-33).   

(5) All fiber photometry recordings were conducted in male mice. Given the sex differences observed in associative learning, the authors could expand the study to include dHPC responses in females during both preconditioning and conditioning sessions. 

We appreciate the comment of the Reviewer. Indeed, thanks to other comments made by other Reviewers in this revision (see Point 1 of Reviewer #2), we are not still sure that we have an optimal protocol to study mediated learning in female mice due to sexspecific changes related to fear generalization. Thus, the revised version of the manuscript, although highlighting these sex differences in behavioral performance (see Supplementary Figure 2), is more focused in male mice and, accordingly, all photometry or chemogenetic experiments are performed exclusively using male mice. In future studies, once we would be sure to have a sensory preconditioning paradigm working in female mice, it will be very interesting to study if the same hippocampal mechanisms mediating this behavior in male mice are also observed in female mice. 

Minor Comments: 

(1) In the right panel of Figure 2A, females received only one conditioning session, so the "x2" should be corrected to "x1" conditioning to accurately reflect the data. 

We thank the Reviewer for the comment that has been addressed in the revised version of the manuscript.  

(2) The overall presentation of Figure 3 could be improved. For example, the y-axis in Panel B could be cut to a maximum of 3 rather than 6, which would better highlight the response data. Alternatively, including heatmap representations of the z-score responses could enhance clarity and visual impact.  

We thank the Reviewer for the comment that has been addressed providing a new format for Figures 2 and 3 in the revised version of the manuscript.   

(3) There are several grammatical errors throughout the manuscript. It is recommended that the authors use a grammar correction tool to improve the overall writing quality and readability.  

We have tried to correct the grammar through all the manuscript.  

Reviewer #2 (Recommendations for the authors):  

(1) In the abstract the authors write that sensory preconditioning requires the "repeated and simultaneous presentation of two low-salience stimuli such as a light and a tone". Previous research has shown that sensory preconditioning can still occur if the two stimuli are presented serially, rather than simultaneously. Further, the tone and the light are not necessarily "low-salience", for example, they can be loud or bright. It would be better to refer to them as innocuous. 

In the revised version of the abstract, we have included the modifications suggested by the Reviewer.   

(2) The authors develop a novel automated tool for assessing freezing behaviour in mice that correlates highly with both manual freezing and existing, open-source freeze estimation software (ezTrack). The authors should explain how the new program differs from ezTrack, or if it provides any added benefit over this existing software. 

We have added new information in the Results Section (Page 10, Lines 13-20 to better explain how the new tool to quantify freezing could improve existing software.  

(3) In Experiment 1, the authors report a sex difference in levels of freezing between male and female mice when they are only given one session of sensory preconditioning. This should be supported by a statistical comparison of levels of freezing between male and female mice. 

Based on the new results obtained with female mice, we have decided to remove the original Figure 1 of the manuscript as it is not meaningful to compare male and female mediated learning response if we do not have an optimal protocol in female mice.  

(4) Why did the authors choose to vary the duration of the stimuli across preconditioning, conditioning, and testing? During preconditioning, the light-tone compound was 30s, in conditioning the light was 10s, and at test both stimuli were presented continuously for 3 min. Did the level of freezing vary across the three-minute probe session? There is some evidence that rodents can learn the timing of stimuli and it may be the case that freezing was highest at the start of the test stimulus, when it most closely resembled the conditioned stimulus. 

Differences in cue exposure between the preconditioning phase and the test phase were decided based on important differences between previous protocols used in rats compared to how mice are responding. Indeed, mice were not able to adapt their behavioral responses when shorter time windows exposing the cue were used as it clearly happens with rats1. In addition, we have added a new graph to show the time course of the behavioral responses (see Figure 1 and 4 and Supplementary Figure 2) that correlate with the quantification of freezing responses shown by the percentage of freezing during ON and OFF periods.   

(5) The title of Experiment 1 "Female and male mice show mediated learning using an auditory-visual sensory preconditioning task" - this experiment does not demonstrate mediated learning; it merely shows that animals will freeze more in the presence of a stimulus as compared with no stimulus. This experiment lacks the necessary controls to claim mediated learning (which are presented in Experiment 2) and should therefore be retitled something more appropriate.

As stated above, based on the new results obtained with female mice, we have decided to remove the original Figure 1 of the manuscript as it is not meaningful to compare male and female mediated learning response if we do not have an optimal protocol in female mice.   

(6) In Figure 2, why does the unpaired group show less freezing to the tone than the paired group given that the tone was directly paired with the shock in both groups? 

We believe the Reviewer may have referred to the tone in error (i.e. there are no differences in the freezing observed to the tone) and (s)he might be talking about the freezing induced by the Light in the direct learning test. In this case, it is true that the direct learning (e.g. percentage of freezing) seems to be slightly lower in the unpaired group compared to the paired one, which could be due to a latent inhibition process caused by the different exposure of cues between paired and unpaired experimental groups. However, the direct learning in both groups is clear and significant and there are no significant differences between them, which makes difficult to extract any further conclusion. 

(7) The stimuli in the design schematics are quite small and hard to see, they should be enlarged for clarity. The box plots also looked stretched and the colour difference between the on and off periods is difficult to discern. 

We have included some important modification to the Figures in order to address the comments made by the Reviewer and improve its quality.   

(8) The authors do not include labels for the experimental groups (paired, unpaired, no shock) in Figures 2B, 2D, 2C, and 2E. This made it very difficult to interpret the figure.  

According to this suggestion, Figure 2 has been changed accordingly. 

(9) The levels of freezing during conditioning should be presented for all experiments.  

We have generated a new Supplementary Figure 9 to show the freezing levels during conditioning sessions. 

(10) In the final experiment, the authors wrote that mice were injected with J60 or saline, but I could not find the data for the saline animals.  

In the Results and Methods section, we have included a sentence to better explain this issue. In addition, we have added a new Supplementary Figure 7 to show the performance of all control groups.  

(11) Please list the total number of animals (per group, per sex) for each experiment.  

In the revised version of the manuscript, we have added this information in each Figure Legend.  

Reviewer #3 (Recommendations for the authors): 

I found this study very interesting, despite a few weaknesses. I have several minor comments to add, hoping that it would improve the manuscript: 

(1) The terminology used is not always appropriate/consistent. I would use "freely moving fiber photometry" or simply "fiber photometry" as calcium imaging conventionally refers to endoscopic or 2-photon calcium imaging. 

We thank the Reviewer for this comment that has been addressed and corrected in the revised version of the manuscript. 

(2) "Dorsal hippocampus mediates light-tone sensory preconditioning task in mice" suggests that a brain region mediates a task. I would rather suggest, e.g. "Dorsal hippocampus mediates light-tone association in mice" 

We thank the Reviewer for this comment that has been addressed and corrected in the revised version of the manuscript.

(3) As you are using low-salience stimuli, it would be better to also inform the readership with the light intensity used for the light cue, for replicability purposes. 

In the Methods section (Page 5, Line 30), we have added new information regarding the visual stimuli used. 

(4) If the authors didn't use a background noise during the probe tests, the tone cue could have been perceived as being louder/clearer by mice. Couldn't it have inflated the freezing response for the tone cue?  

This is an interesting comment made by the Reviewer although we do not have any data to directly answer his/her suggestion. However, the presence of the Background noise resulted necessary to set up the protocol and to change different aspects of the context through all the paradigm, which was necessary to avoid fear generalization in mice. In addition, as demonstrated before [6] , the presence of background noise is important to avoid that other auditory cue (i.e. tone) could induce fear responses by itself as the transition of noise to silence is a signal to danger for animals. 

(5) "salience" is usually used for the intensity of a stimulus, not for an association or pairing. Rather, we usually refer to the strength of an association. 

We thank the Reviewer for this comment that has been addressed and corrected in the revised version of the manuscript.

(6) Figure 3, panel A. "RCaMP Neurons", maybe "Pan-Neurons" would be more appropriate, as PV+ inter-neurons are also neurons. 

We thank the Reviewer for this comment that has been corrected accordingly.

(7) Figure 4, panel A, please add the AAV injected, and the neurons labelled in your example slice. 

We thank the Reviewer for this comment that has been corrected accordingly.

References

(1) Wong, F. S., Westbrook, R. F. & Holmes, N. M. 'Online' integration of sensory and fear memories in the rat medial temporal lobe. Elife 8 (2019). https://doi.org:10.7554/eLife.47085

(2) Prendergast, B. J., Onishi, K. G. & Zucker, I. Female mice liberated for inclusion in neuroscience and biomedical research. Neurosci Biobehav Rev 40, 1-5 (2014). https://doi.org:10.1016/j.neubiorev.2014.01.001

(3) Becker, J. B., Prendergast, B. J. & Liang, J. W. Female rats are not more variable than male rats: a meta-analysis of neuroscience studies. Biol Sex Differ 7, 34 (2016). https://doi.org:10.1186/s13293-016-0087-5

(4) Shansky, R. M. Are hormones a "female problem" for animal research? Science 364,  825-826 (2019). https://doi.org:10.1126/science.aaw7570

(5) Busquets-Garcia, A. et al. Hippocampal CB1 Receptors Control Incidental Associations. Neuron 99, 1247-1259 e1247 (2018). https://doi.org:10.1016/j.neuron.2018.08.014

(6) Pereira, A. G., Cruz, A., Lima, S. Q. & Moita, M. A. Silence resulting from the cessation of movement signals danger. Curr Biol 22, R627-628 (2012). https://doi.org:10.1016/j.cub.2012.06.015

eLife Assessment

This Research Advance manuscript further elucidates the roles of SMC5/6 loader proteins and associated factors in the silencing of extrachromosomal circular DNA by the SMC5/6 complex. While the findings are largely in line with expectations, they are valuable, representing a meaningful advance beyond the recent study from the same laboratories (PMC9708086), validating the previous model that distinct SMC5/6 subcomplexes, SIMC1-SLF2 and SLF1/2, separately control its transcriptional repression and DNA repair activities on extrachromosomal DNA. Solid evidence is presented for a role for SIMC1/SLF2 in localization of the SMC5/6 complex to plasmid DNA, and the distinct requirements as compared to recruitment of SMC5/6 to chromosomal DNA lesions.

Reviewer #1 (Public review):

SMC5/6 is a highly conserved complex able to dynamically alter chromatin structure, playing in this way critical roles in genome stability and integrity that include homologous recombination and telomere maintenance. In the last years, a number of studies have revealed the importance of SMC5/6 in restricting viral expression, which is in part related to its ability to repress transcription from circular DNA. In this context, Oravcova and colleagues recently reported how SMC5/6 is recruited by two mutually exclusive complexes (orthologs of yeast Nse5/6) to SV40 LT-induced PML nuclear bodies (SIMC/SLF2) and DNA lesions (SLF1/2). In this current work, the authors extend this study, providing some new results.

Reviewer #2 (Public review):

Oracová et al. present data supporting a role for SIMC1/SLF2 in silencing plasmid DNA via the SMC5/6 complex. Their findings are of interest, and they provide further mechanistic detail of how the SMC5/6 complex is recruited to disparate DNA elements. In essence, the present report builds on the author's previous paper in eLife in 2022 (PMID: 36373674, "The Nse5/6-like SIMC1-SLF2 complex localizes SMC5/6 to viral replication centers") by showing the role of SIMC1/SLF2 in localisation of the SMC5/6 complex to plasmid DNA, and the distinct requirements as compared to recruitment to DNA damage foci.

Reviewer #3 (Public review):

This study by the Boddy and Otomo laboratories further characterizes the roles of SMC5/6 loader proteins and related factors in SMC5/6-mediated repression of extrachromosomal circular DNA. The work shows that mutations engineered at an AlphaFold-predicted protein-protein interface formed between the loader SLF2/SIMC1 and SMC6 (similar to the interface in the yeast counterparts observed by cryo-EM) prevent co-IP of the respective proteins. The mutations in SLF2 also hinder plasmid DNA silencing when expressed in SLF2-/- cell lines, suggesting that this interface is needed for silencing. SIMC1 is dispensable for recruitment of SMC5/6 to sites of DNA damage, while SLF1 is required, thus separating the functions of the two loader complexes. Preventing SUMOylation (with a chemical inhibitor) increases transcription from plasmids but does not in SLF2-deleted cell lines, indicating the SMC5/6 silences plasmids in a SUMOylation dependent manner. Expression of LT is sufficient for increased expression, and again, not additive or synergistic with SIMC1 or SLF2 deletion, indicating that LT prevents silencing by directly inhibiting 5/6. In contrast, PML bodies appear dispensable for plasmid silencing.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

SMC5/6 is a highly conserved complex able to dynamically alter chromatin structure, playing in this way critical roles in genome stability and integrity that include homologous recombination and telomere maintenance. In the last years, a number of studies have revealed the importance of SMC5/6 in restricting viral expression, which is in part related to its ability to repress transcription from circular DNA. In this context, Oravcova and colleagues recently reported how SMC5/6 is recruited by two mutually exclusive complexes (orthologs of yeast Nse5/6) to SV40 LT-induced PML nuclear bodies (SIMC/SLF2) and DNA lesions (SLF1/2). In this current work, the authors extend this study, providing some new results. However, as a whole, the story lacks unity and does not delve into the molecular mechanisms responsible for the silencing process. One has the feeling that the story is somewhat incomplete, putting together not directly connected results.

Please see the introductory overview above.

(1) In the first part of the work, the authors confirm previous conclusions about the relevance of a conserved domain defined by the interaction of SIMC and SLF2 for their binding to SMC6, and extend the structural analysis to the modelling of the SIMC/SLF2/SMC complex by AlphaFold. Their data support a model where this conserved surface of SIMC/SLF2 interacts with SMC at the backside of SMC6's head domain, confirming the relevance of this interaction site with specific mutations. These results are interesting but confirmatory of a previous and more complete structural analysis in yeast (Li et al. NSMB 2024). In any case, they reveal the conservation of the interaction. My major concern is the lack of connection with the rest of the article. This structure does not help to understand the process of transcriptional silencing reported later beyond its relevance to recruit SMC5/6 to its targets, which was already demonstrated in the previous study.

Demonstrating the existence of a conserved interface between the Nse5/6-like complexes and SMC6 in both yeast and human is foundationally important, not confirmatory, and was not revealed in our previous study. It remains unclear how this interface regulates SMC5/6 function, but yeast studies suggest a potential role in inhibiting the SMC5/6 ATPase cycle. Nevertheless, the precise function of Nse5/6 and its human orthologs in SMC5/6 regulation remain undefined, largely due to technical limitations in available in vivo analyses. The SIMC1/SLF2/SMC6 complex structure likely extends to the SLF1/2/SMC6 complex, suggesting a unifying function of the Nse5/6-like complexes in SMC5/6 regulation, albeit in the distinct processes of ecDNA silencing and DNA repair. There have been no studies to date (including this one) showing that SIMC1-SLF2 is required for SMC5/6 recruitment to ecDNA. Our previous study showed that SIMC1 was needed for SMC5/6 to colocalize with SV40 LT antigen at PML NBs. Here we show that SIMC1 is required for ecDNA repression, in the absence of PML NBs, which was not anticipated.

(2) In the second part of the work, the authors focus on the functionality of the different complexes. The authors demonstrate that SMC5/6's role in transcription silencing is specific to its interaction with SIMC/SLF2, whereas SMC5/6's role in DNA repair depends on SLF1/2. These results are quite expected according to previous results. The authors already demonstrated that SLF1/2, but not SIMC/SLF2, are recruited to DNA lesions. Accordingly, they observe here that SMC5/6 recruitment to DNA lesions requires SLF1/2 but not SIMC/SLF2. Likewise, the authors already demonstrated that SIMC/SLF2, but not SLF1/2, targets SMC5/6 to PML NBs. Taking into account the evidence that connects SMC5/6's viral resistance at PML NBs with transcription repression, the observed requirement of SIMC/SLF2 but not SLF1/2 in plasmid silencing is somehow expected. This does not mean the expectation has not to be experimentally confirmed. However, the study falls short in advancing the mechanistic process, despite some interesting results as the dispensability of the PML NBs or the antagonistic role of the SV40 large T antigen. It had been interesting to explore how LT overcomes SMC5/6-mediated repression: Does LT prevent SIMC/SLF2 from interacting with SMC5/6? Or does it prevent SMC5/6 from binding the plasmid? Is the transcription-dependent plasmid topology altered in cells lacking SIMC/SLF2? And in cells expressing LT? In its current form, the study is confirmatory and preliminary. In agreement with this, the cartoons modelling results here and in the previous work look basically the same.

Our previous study only examined the localization of SLF1 and SIMC1 at DNA lesions. The localization of these subcomplexes alone should not be used to define their roles in SMC5/6 localization. Indeed, the field is split in terms of whether Nse5/6-like complexes are required for ecDNA binding/loading, or regulation of SMC5/6 once bound. 

We agree, determining the potential mechanism of action of LT in overcoming SMC5/6-based repression is an important next step. We believe it is unlikely due to blocking of the SMC5/6SIMC1/SLF2 interface, since SIMC1-SLF2 is required for SMC5/6 to localize at LT-induced foci. It will require the identification of any direct interactions with SMC5/6 subunits, and better methods for assessing SMC5/6 loading and activity on ecDNAs. Unlike HBx, Vpr, and BNRF1 it does not appear to induce degradation of SMC5/6, making it a more complex and interesting challenge. Also, the dispensability of PML NBs in plasmid silencing versus viral silencing raises multiple important questions about SMC5/6’s repression mechanism. 

(3) There are some points about the presented data that need to be clarified.

Thank you, we have addressed these points below, within the Recommendations for authors section.

Reviewer #2 (Public review):

Oracová et al. present data supporting a role for SIMC1/SLF2 in silencing plasmid DNA via the SMC5/6 complex. Their findings are of interest, and they provide further mechanistic detail of how the SMC5/6 complex is recruited to disparate DNA elements. In essence, the present report builds on the author's previous paper in eLife in 2022 (PMID: 36373674, "The Nse5/6-like SIMC1-SLF2 complex localizes SMC5/6 to viral replication centers") by showing the role of SIMC1/SLF2 in localisation of the SMC5/6 complex to plasmid DNA, and the distinct requirements as compared to recruitment to DNA damage foci. Although the findings of the manuscript are of interest, we are not yet convinced that the new data presented here represents a compelling new body of work and would better fit the format of a "research advance" article. In their previous paper, Oracová et al. show that the recruitment of SMC5/6 to SV40 replication centres is dependent on SIMC1, and specifically, that it is dependent on SIMC1 residues adjacent to neighbouring SLF2.

We agree. We submitted this manuscript as a “Research Advance”, not as a standalone research article, given that it is an extension of our previous “Research Article” (1).

Other comments

(1) The mutations chosen in Figure 1 are quite extensive - 5 amino acids per mutant. In addition, they are in many cases 'opposite' changes, e.g., positive charge to negative charge. Is the effect lost if single mutations to an alanine are made?

The mutations were chosen to test and validate the predicted SIMC1-SLF2-SMC6 structure i.e. the contact point between the conserved patch of SIMC1-SLF2 and SMC6. Multiple mutations and charge inversions increased the chance of disrupting the extensive interface. In this respect, the mutations were successful and informative, confirming the requirement of this region in specifically contacting SMC6. Whilst alanine scanning mutations are possible, we believe that they would not add to, or detract from, our validation of the predicted SIMC1-SLF2-SMC6 interface.

(2) In Figure 2c, it isn't clear from the data shown that the 'SLF2-only' mutations in SMC6 result in a substantial reduction in SIMC1/SLF2 binding.

To clarify the difference between wild-type and SLF2-only mutations in SIMC1-SLF2 interaction, we have performed an image volume analysis. This shows that the SLF2-facing SMC6 mutant reduces its interaction with SIMC1 (to 44% of WT) and SLF2 (to 21% of WT). The reduction in both SIMC1 and SLF2 interaction with SMC6 SLF2-facing mutant is expected, since SIMC1 and SLF2 are an interdependent heterodimer.  

Author response table 1.

(3) In the GFP reporter assays (e.g. Figure 3), median fluorescence is reported - was there any observed difference in the percentage of cells that are GFP positive?

Yes, as expected when the GFP plasmid is not actively repressed, the percent of GFP positive cells differs in each cell line – in the same trend as GFP intensity

(4) The potential role of the large T antigen as an SMC5/6 evasion factor is intriguing. However, given the role of the large T antigen as a transcriptional activator, caution is required when interpreting enhanced GFP fluorescence. Antagonism of the SMC5/6 complex in this context might be further supported by ChIP experiments in the presence or absence of large T. Can large T functionally substitute for HBx or HIV-Vpr?

We agree, the potential role of LT in SMC5/6 antagonism is interesting. We did state in the text “While LT is known to be a promiscuous transcriptional activator (2,3) that does not rule out a co-existing role in antagonizing SMC5/6. Indeed, these findings are reminiscent of HBx from HBV and Vpr of HIV-1, both of which are known promiscuous transcriptional activators that also directly antagonize SMC5/6 to relieve transcriptional repression (4-10).“ We have tried ChIP experiments, but found these to be unreliable in assessing SMC5/6 association with plasmid DNA. Given the many disparate targets of LT, HBx and Vpr (other than SMC5/6), it seems unlikely that LT could functionally substitute for HBx and Vpr in supporting HBV and HIV-1 infections. Whilst certainly an interesting future question, we believe it is beyond the scope of this study.

(5) In Figure 5c, the apparent molecular weight of large T and SMC6 appears to change following transfection of GFP-SMC5 - is there a reason for this?

We are not certain as to what causes the molecular weight shift, but it is not specifically related to GFPSMC5 transfection. Rather, it appears to be a general effect of the pulldown. Indeed, a very weak “background” band of LT is seen in the GFP only pulldown, which also runs at a “higher” molecular weight, as in the GFP-SMC5 pulldown. We believe that the effect is instead related to gel mobility in the wells that contain post pulldown proteins and different buffers. We have also seen similar effects using different protein-protein interaction pairs. 

Reviewer #3 (Public review):

Summary:

This study by the Boddy and Otomo laboratories further characterizes the roles of SMC5/6 loader proteins and related factors in SMC5/6-mediated repression of extrachromosomal circular DNA. The work shows that mutations engineered at an AlphaFold-predicted protein-protein interface formed between the loader SLF2/SIMC1 and SMC6 (similar to the interface in the yeast counterparts observed by cryo-EM) prevent co-IP of the respective proteins. The mutations in SLF2 also hinder plasmid DNA silencing when expressed in SLF2-/- cell lines, suggesting that this interface is needed for silencing. SIMC1 is dispensable for recruitment of SMC5/6 to sites of DNA damage, while SLF1 is required, thus separating the functions of the two loader complexes. Preventing SUMOylation (with a chemical inhibitor) increases transcription from plasmids but does not in SLF2-deleted cell lines, indicating the SMC5/6 silences plasmids in a SUMOylation dependent manner. Expression of LT is sufficient for increased expression, and again, not additive or synergistic with SIMC1 or SLF2 deletion, indicating that LT prevents silencing by directly inhibiting 5/6. In contrast, PML bodies appear dispensable for plasmid silencing.

Strengths:

The manuscript defines the requirements for plasmid silencing by SMC5/6 (an interaction of Smc6 with the loader complex SLF2/SIMC1, SUMOylation activity) and shows that SLF1 and PML bodies are dispensable for silencing. Furthermore, the authors show that LT can overcome silencing, likely by directly binding to (but not degrading) SMC5/6.

Weaknesses:

(1) Many of the findings were expected based on recent publications.

There have been no manuscripts describing the role of SIMC1-SLF2 in ecDNA silencing. There have been studies describing SLF2’s roles in ecDNA silencing, but these suggested SLF2 had an SLF1 independent role, with no mention of an alternate Nse5-like cofactor. Our earlier study in eLife (1) described the identification of SIMC1 as an Nse5-like cofactor for SLF2 but did not test potential roles of the complex in ecDNA silencing. Also, the apparent dispensability of PML NBs in plasmid silencing (in U2OS cells) was unexpected based on recent publications. Finally, SV40 LT has not previously been implicated in SMC5/6 inhibition, which may occur through novel mechanisms.

(2) While the data are consistent with SIMC1 playing the main function in plasmid silencing, it is possible that SLF1 contributes to silencing, especially in the absence of SIMC1. This would potentially explain the discrepancy with the data reported in ref. 50. SLF2 deletion has a stronger effect on expression than SIMC1 deletion in many but not all experiments reported in this manuscript. A double mutant/deletion experiments would be useful to explore this possibility.

It is interesting to note that the data in ref. 50 (11) is also at odds with that in ref. 45 (8) in terms of defining a role for SLF1 in the silencing of unintegrated HIV-1 DNA. The Irwan study showed that SLF1 deficient cells exhibit increased expression of a reporter gene from unintegrated HIV-1, whereas the Dupont study found that SLF1 deletion, unlike SLF2 deletion, has no effect. It is unclear what the basis of this discrepancy is. In line with the Dupont study, we found no effect of SLF1 deletion on plasmid expression (Figure 4B), whereas SLF2 deletion increased reporter expression (Figure 3A/B). It is possible that SLF1 could support some plasmid silencing in the absence of SIMC1, especially considering the gross structural similarity in their C-terminal Nse5-like domains. However, we have been unable to generate double-knockout SIMC1 and SLF1 cells to test such a possibility, and shSLF1 has been ineffective. 

(3) SLF2 is part of both types of loaders, while SLF1 and SIMC1 are specific to their respective loaders. Did the authors observe differences in phenotypes (growth, sensitivities to DNA damage) when comparing the mutant cell lines or their construction? This should be stated in the manuscript.

We have not observed significant differences in the growth rates of each cell line, and DNA damage sensitivities are as yet untested.   

(4) It would be desirable to have control reporter constructs located on the chromosome for several experiments, including the SUMOylation inhibition (Figures 5A and 5-S2) and LT expression (Figure 5D) to exclude more general effects on gene expression.

We have repeated all GFP reporter assays using integrated versus episomal plasmid DNA. A seminal study by Decorsière et al. (6) showed that SMC5/6 degradation by HBx of HBV increased transcription of episomal but not chromosomally integrated reporters. In line with this data, the deletion of SLF2 does not notably impact the expression of our GFP reporter construct when it is genomically integrated (Figure 3—figure supplement 1C).  

Somewhat surprisingly, given the generally transcriptionally repressive roles of SUMO, inhibition of the SUMO pathway with SUMOi did not significantly impact the expression of our genomically integrated GFP reporter, versus the episomal plasmid (Figure 5—figure supplement 1C). Finally, the expression of SV40 LT, which enhances plasmid reporter expression (Figure 5D), also did not notably affect expression of the same reporter when located in the genome (Figure 5—figure supplement 3B). This is an interesting result, which is in line with an early study showing that HBx of HBV induces transcription from episomal, but not chromosomally integrated reporters (12). This further suggests that SV40 LT acts similarly to other early viral proteins like HBx and Vpr to counteract or bypass SMC5/6 restriction, amongst their multifaceted functions. Clearly, further analyses are needed to define mechanisms of LT in counteracting SMC5/6, but they do not appear to include complex degradation as seen with HBx and Vpr.  

(5) Figure 5A: There appears to be an increase in GFP in the SLF2-/- cells with SUMOi? Is this a significant increase?

No significant difference was found between WT, SIMC1-/- or SLF2-/- when treated with SUMOi (p>0.05). The p-value is 0.0857 (when comparing SLF2-/- to WT in the SUMOi condition) This is described in the figure legend to Figure 5.

(6) The expression level of SFL2 mut1 should be tested (Figure 3B).

Full length SLF2 (WT or mutants) has been undetectable by western analyses. However, truncated SLF2 mut1 expresses well and binds SIMC1 but not SMC6 (Figure 1C). Moreover, full length SLF2 mut1 expression was confirmed by qPCR – showing a somewhat higher expression level than SLF2 WT (Figure 3—figure supplement 1B).  

Reviewer #1 (Recommendations for the authors):

There are some points about the presented data that need to be clarified.

(1) Figures 3, 4B, and 5. The authors should rule out the possibility that the reported effects on transcription were due to alterations in plasmid number. This is particularly important, taking into account the importance of SMC5/6 in DNA replication.

We used qPCR to assess plasmid copy number versus genomic DNA in our cell lines, testing at 72 hours post transfection to avoid any impact of cytosolic DNA (13). Our qPCR data show that there is no significant impact on plasmid copy number across our cell lines i.e. WT and SLF2 null.  SMC5/6 has a positive role in DNA replication progression on the genome (e.g. (14)), so loss of SMC5/6 “targeting” in SIMC1 and SLF2 null cells would be unlikely to promote replication fork progression per se. 

(2) Figure S1A. In contrast to the statement in the text, the SIMC1-combo control is affected in its binding to SLF2; however, it is not affected in its binding to SMC6. This is somehow unexpected because it suggests that the solenoid-like structure is not required for SMC6 binding, just specific patches at either SIMC or SLF2. This should be commented on.

We appreciate the reviewer’s observation regarding the discrepancy between Figure S1A and the text. This was our oversight. The data show that SLF2 recovery was reduced in the pull-down with the SIMC1 combo control mutant, while SLF2 expression was unchanged. Because SLF2 or SIMC1 variants that fail to associate typically show poor expression (1), these findings suggest that the SIMC1 combo control mutant associates with SLF2, albeit more weakly. Since the mutations were introduced into surface residues of SIMC1, it is not immediately clear how they would weaken the interaction or destabilize the complex. In contrast, SMC6 was fully recovered with the SIMC1 combo control mutant, indicating that the SIMC1–SMC6 interaction remains stable without stoichiometric SLF2. This may reflect direct recognition of a SIMC1 binding epitope or stabilization of its solenoid structure by SMC6, although this interpretation remains uncertain given the unstable nature of free SIMC1 and SLF2. Alternatively, SMC6 may have co-sedimented with the SIMC1 combo control mutant together with SLF2, which was initially retained but subsequently lost during washing, whereas SMC6 remained due to its limited solubility in the absence of other SMC5/6 subunits. While further mechanistic analysis will require purified SMC5/6 components, our data support the AlphaFold-based model by demonstrating that SIMC1 mutations on the non–SMC6-contacting surface retain association with SMC6. The text has been revised accordingly.

(3) The SLF2-only mutant has alterations that affect interactions with both SLF2 and SIMC1. Is it not another Mixed mutant?

We appreciate the reviewer’s observation regarding the discrepancy between the mutant name (“SLF2only”) and its description (“while N947 forms salt bridges with SIMC1”). The previous statement was inaccurate due to a misinterpretation of several AlphaFold models. Across these models, the SIMC1– SLF2 interface residues remain largely consistent, but the SIMC1 residue R470 exhibits positional variability—contacting N947 in some models but not in others. Given this variability and the absence of an experimental structure, we have revised the text to avoid overinterpretation. Because the N947 side chain is oriented toward SLF2 and consistently forms polar contacts with the H1148 side chain and G1149 backbone, we have renamed this mutant “SLF2-facing,” which more accurately describes its modeled environment. The other mutants are likewise renamed “SIMC1-facing” and “SIMC1–SLF2groove-facing,” providing a clearer and more consistent description of the interface.

(4) The SLF2-only mutant still displays clear interactions with SMC6. Can this be explained with the AlphaFold model?

SIMC1 may contribute more substantially to SMC6 binding than SLF2, consistent with our mutagenesis results. However, the energetic contributions of individual residues or proteins cannot be quantitatively inferred from structural models alone. Comprehensive experimental and computational analyses would be required to address this point.

(5) The conclusions about the role of SUMOylation are vague; it is already known that its general effect on transcription repression, and the authors already demonstrated that SIMC interacts with SUMO pathway factors. Concerning the epistatic effect, the experiment should be done at a lower inhibitor concentration; at 100 nM there is not much margin to augment according to the kinetics analysis in Figure S5.

The SUMO pathway is indeed thought to be generally repressive for transcription. Notably, in response to a suggestion from Reviewer 3 (public review point 4), we have repeated several of our GFP expression assays using cells with the GFP reporter plasmid integrated into the genome (please see Figure 3—figure supplement 1C; Figure 5—figure supplement 1C; Figure 5—figure supplement 3B). This type of integrated reporter does not show elevated expression following inhibition of the SMC5/6 complex, unlike ecDNAs (6,10). Interestingly, SUMOi, LT expression, and SLF2 knockout also did not notably impact the expression of our integrated GFP reporter (Figure 3—figure supplement 1C; Figure 5—figure supplement 1C; Figure 5—figure supplement 3B, unlike that of the plasmid (ecDNA) reporter. Given the “general” inhibitory effect of SUMO on transcription, the SUMOi result was not expected, and it opens further interesting avenues for study. 

In Figure 5—figure supplement 1A, 100 nM SUMOi increases reporter expression well below the highest SUMOi dose. We believe that the ~3-4 fold induction of GFP expression in SLF2 null cells, if independent of SUMOylation, should further increase GFP expression. The impact of SUMOylation on GFP reporter expression remains “vague”, but our data indicate that SMC5/6 operates within SUMO’s “umbrella” function and provides a starting point for more mechanistic dissection. 

(6) Figure 5C. Why is the size different between Input versus GFP-PD?

Please see our response to this question above: reviewer 2, point (5)

Reviewer #2 (Recommendations for the authors):

If further data could be provided to extend on that which is presented, then publication as a 'standalone research article' may be appropriate, but not in its present form.

We submitted this manuscript as a “Research Advance” not as a standalone research article, given that it was an extension of our previous research article (1).

Reviewer #3 (Recommendations for the authors):

(1) The term 'LT' should be defined in the title

We have updated the title accordingly.  

(2) This reviewer found the nomenclature of the SMC6 mutants confusing (SIMC1-only...). Either rephrase or define more clearly in the text and the figures.

We agree with the reviewer and have renamed the mutants as “SIMC1-facing”, “SLF2-facing,”, and “SIMC1–SLF2-groove-facing”.

(3) The authors could better emphasize that LT blocks silencing in trans (not only on its cognate target sequence in cis). This is consistent with the observed direct binding to SMC5/6.

We appreciate the suggestion to further emphasize the impact of LT on plasmid silencing. We did not want to overstate its impact at this time because we do not know if it directly binds SMC5/6 or indeed affects SMC5/6 function more broadly. LT expression like HBx, does cause induction of a DNA damage response, but we cannot at this point tie that response to SMC5/6 inhibition alone.

(4) Figure 5 S1: the merge looks drastically different. Is DAPI omitted in the wt merge image?

Thank you for noting this issue. We have corrected the image, which was impacted by the use of an underexposed DAPI image.  

(5) Figure 1: how is the structure in B oriented relative to A? A visual guide would be helpful.

We have added arrows to indicate the view orientation and rotational direction to turn A to B.

(6) Line 126, unclear what "specificity" here means.

We have revised the sentence without this word, which now starts with “To confirm the SIMC1-SMC6 interface, we introduced….”

(7) Line 152, The statement implies that the conserved residues are needed for loader subunits interactions ('mediating the SIMC1-SLF2 interaction"). Does Figure 1C not show that the residues are not important? Please clarify.

Thank you for noting this writing error. We have corrected the sentence to provide the intended meaning. It now reads "Collectively, these results confirm that the conserved surface patch of SIMC1SLF2 is essential for SMC6 binding.” 

References

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(8) Dupont L, Bloor S, Williamson JC, Cuesta SM, Shah R, Teixeira-Silva A, Naamati A, Greenwood EJD, Sarafianos SG, Matheson NJ, Lehner PJ. The SMC5/6 complex compacts and silences unintegrated HIV-1 DNA and is antagonized by Vpr. Cell Host Microbe. 2021;29(5):792-805 e6. PMCID: PMC8118623

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eLife Assessment

This paper provides potentially valuable insight into why memory consolidation may differ between children (5-7 years of age) and adults. The work hints at developmental differences in neural engagement during the retrieval of recent and remote memories. However, there are several major concerns with the analyses not alleviated by included controls, and as such the evidence supporting the authors' main claims remains incomplete.

Reviewer #2 (Public review):

Summary:

Schommartz et al. present a manuscript characterizing neural signatures of reinstatement during cued retrieval of middle-aged children compared to adults. The authors utilize a paradigm where participants learn the spatial location of semantically related item-scene memoranda which they retrieve after short or long delays. The paradigm is especially strong as the authors include novel memoranda at each delayed time point to make comparisons across new and old learning. In brief, the authors find that children show more forgetting than adults, and adults show greater engagement of cortical networks after longer delays as well as stronger item-specific reinstatement. Interestingly, children show more category-based reinstatement, however, evidence supports that this marker may be maladaptive for retrieving episodic details. The question is extremely timely both given the boom in neurocognitive research on the neural development of memory, and the dearth of research on consolidation in this age group. Also, the results provide novel insights into why consolidation processes may be disrupted in children.

Comments on latest version:

I carefully reviewed not only the responses to my own reviews as well as those raised by the other reviewers. While they addressed some of the concerns raised in the process, I think many substantive concerns remain.

While I appreciate the authors sub-sample analysis to control for re-exposure to stimuli in children versus adults, the authors only performed this analysis on memory performance and univariate activation, but they did not run this on the main focus of interest which was the pattern analysis. I think this is critical to run as these measures would be the ones most sensitive to repetition and are the foundation for the major claims of the manuscript.

Also, I still agree that the authors should do an analysis the subsets the number of trials. While they highlight problems with the loss of statistical power and introduced variability, it is these two very same factors that could be potentially driving these differences.

As part of their efforts to resolve some concerns about their analysis pipeline, the authors show that similar effects do not emerge for incorrectly remembered items. While this is helpful, it would be important to do direct comparisons of subsequently remembered and forgotten items.

There is a major concern that the white matter control ROIs are showing session effects, and even the ones that are for the contrasts of interest are marginally significant (p=0.08). This raises significant concerns about the ability to interpret the authors' main signal of interest. While I appreciate many of the other control analyses, this one analysis is quite worrisome.

Similarly, for the item related analysis, the results should look absolutely different, but the authors are showing effects of p-values that are hovering around significance. Indeed, for these analyses to be true controls, perhaps they should directly control across conditions (i.e., use the item reinstatement as a confound control statistically).

The across run comparisons are a nice addition to the revision, and although they are similar to within conditions, I would recommend when combining these signals there is a factor included for within versus across run comparisons, and the authors show that there are no interactions with this feature.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review): 

Summary: 

This paper by Schommartz and colleagues investigates the neural basis of memory reinstatement as a function of both how recently the memory was formed (recent, remote) and its development (children, young adults). The core question is whether memory consolidation processes as well as the specificity of memory reinstatement differ with development. A number of brain regions showed a greater activation difference for recent vs. remote memories at the long versus shorter delay specifically in adults (cerebellum, PHG, LOC). A different set showed decreases in the same comparison, but only in children (precuneus, RSC). The authors also used neural pattern similarity analysis to characterize reinstatement, though still in this revised paper I have substantive concerns about how the analyses were performed. While scene-specific reinstatement decreased for remote memories in both children and adults, claims about its presence cannot be made given the analyses. Gist-level reinstatement was observed in children but not adults, but I also have concerns about this analysis. Broadly, the behavioral and univariate findings are consistent with the idea memory consolidation differs between children and adults in important ways, and takes a step towards characterizing how.

Strengths: 

The topic and goals of this paper are very interesting. As the authors note, there is little work on memory consolidation over development, and as such this will be an important data point in helping us begin to understand these important differences. The sample size is great, particularly given this is an onerous, multi-day experiment; the authors are to be commended for that. The task design is also generally well controlled, for example as the authors include new recently learned pairs during each session.  

Weaknesses: 

As noted above and in my review of the original submission, the pattern similarity analysis for both item and category-level reinstatement were performed in a way that is not interpretable given concerns about temporal autocorrelation within scanning run.Unfortunately these issues remain of concern in this revision because they were not rectified. Most of my review focuses on this analytic issue, though I also outline additional concerns. 

(1) The pattern similarity analyses are largely uninterpretable due to how they were performed. 

(a) First, the scene-specific reinstatement index: The authors have correlated a neural pattern during a fixation cross (delay period) with a neural pattern associated with viewing a scene as their measure of reinstatement. The main issue with this is that these events always occurred back-to-back in time. As such, the two patterns will be similar due simply to the temporal autocorrelation in the BOLD signal. Because of the issues with temporal autocorrelation within scanning run, it is always recommended to perform such correlations only across different runs. In this case, the authors always correlated patterns extracted from the same run, and which moreover have temporal lags that are perfectly confounded with their comparison of interest (i.e., from Fig 4A, the "scene-specific" comparisons will always be back-to-back, having a very short temporal lag; "set-based" comparisons will be dispersed across the run, and therefore have a much higher lag). The authors' within-run correlation approach also yields correlation values that are extremely high - much higher than would be expected if this analysis was done appropriately. The way to fix this would be to restrict the analysis to only cross-run comparisons, which is not possible given the design. 

To remedy this, in the revision the authors have said they will refrain from making conclusions about the presence of scene-specific reinstatement (i.e., reinstatement above baseline). While this itself is an improvement from the original manuscript, I still have several concerns. First, this was not done thoroughly and at times conclusions/interpretations still seem to imply or assume the presence of scene reinstatement (e.g., line 979-985, "our research supports the presence of scene-specific reinstatement in 5-to-7-year-old children"; line 1138). 

We thank the reviewers for pointing out that there are inconsistencies in our writing. We agree that we cannot make any claims about the baseline level of scene-specific reinstatement. To reiterate, our focus is on the changes in reinstatement over time (30 minutes, 24 hours, and two weeks after learning), which showed a robust decrease. Importantly, scenespecific reinstatement indices for recent items — tested on different days — did not significantly differ, as indicated by non-significant main effects of Session (all p > .323) and Session x ROI interactions (all p > .817) in either age group. This supports our claim that temporal autocorrelation is stable and consistent across conditions and that the observed decline in scene-specific reinstatement reflects a time-dependent change in remote retrieval. We have revised the highlighted passages, accordingly, emphasizing the delay-related decrease in scene-specific reinstatement rather than its absolute magnitude. 

Second, the authors' logic for the neural-behavioural correlations in the PLSC analysis involved restricting to regions that showed significant reinstatement for the gist analysis, which cannot be done for the analogous scene-specific reinstatement analysis. This makes it challenging to directly compare these two analyses since one was restricted to a small subset of regions and only children (gist), while scene reinstatement included both groups and all ROIs. 

We thank the reviewer for pointing this out and want to clarify that it was not our intention to directly compare these analyses. For the neural-behavioral correlations, we included only those regions identified based on gist-like representations baseline, whereas for scene-specific reinstatement, we included all regions due to the absence of such a baseline. The primary aim of the PLSC analysis was to identify a set of regions that, after a stringent permutation and bootstrapping procedure, form a latent variable that explains a significant proportion of variance in behavioral performance across all participants. 

Third, it is also unclear whether children and adults' values should be directly comparable given pattern similarity can be influenced by many factors like motion, among other things. 

We thank the reviewer for raising this important point. In our multivariate analysis, we included confounding regressors specifically addressing motion-related artefacts. Following recent best practices for mitigating motion-related confounding factors in both adult and pediatric fMRI data (Ciric et al., 2017; Esteban et al., 2020; Jones et al., 2021; Satterthwaite et al., 2013), we implemented the most effective motion correction strategies. 

Importantly, our group × session interaction analysis focuses on relative changes in reinstatement over time rather than comparing absolute levels of pattern similarity between children and adults. This approach controls for potential baseline differences and instead examines whether the magnitude of delay-related changes differs across groups. We believe this warrants the comparison and ensures that our conclusions are not driven by group-level differences in baseline similarity or motion artifacts.

My fourth concern with this analysis relates to the lack of regional specificity of the effects. All ROIs tested showed a virtually identical pattern: "Scene-specific reinstatement" decreased across delays, and was greater in children than adults. I believe control analyses are needed to ensure artifacts are not driving these effects. This would greatly strengthen the authors' ability to draw conclusions from the "clean" comparison of day 1 vs. day 14. (A) The authors should present results from a control ROI that should absolutely not show memory reinstatement effects (e.g., white matter?). Results from the control ROI should look very different - should not differ between children and adults, and should not show decreases over time. 

(C) If the same analysis was performed comparing the object cue and immediately following fixation (rather than the fixation and the immediately following scene), the results should look very different. I would argue that this should not be an index of reinstatement at all since it involves something presented visually rather than something reinstated (i.e., the scene picture is not included in this comparison). If this control analysis were to show the same effects as the primary analysis, this would be further evidence that this analysis is uninterpretable and hopelessly confounded. 

We appreciate the reviewer’s suggestion to strengthen the interpretation of our findings by including appropriate control analyses to rule out non-memory-related artifacts. In response, we conducted several control analyses, detailed below, which collectively support the specificity of the observed reinstatement effects. The report of the results is included in the manuscript (line 593-619).

We checked that item reinstatement for incorrectly remembered trial did not show any session-related decline for any ROI. This indicates that the reinstatement for correctly remembered items is memory-related (see Fig. S5 for details). 

We conducted additional analyses on three subregions of the corpus callosum (the body, genu, and splenium). The results of the linear mixed-effects models revealed no significant group effect (all p > .426), indicating no differences between children and adults. In contrast, all three ROIs showed a significant main effect of Session (all p < .001). However, post hoc analyses indicated that this effect was driven by differences between the recent and the Day 14 remote condition. The main contrasts of interest – recent vs. Day 1 remote and Day 1 remote vs. Day 14 remote – were not significant (all p > .080; see Table S10.4), suggesting that, unlike in other ROIs, there was no delay-related decrease in scene-specific reinstatement in these white matter regions.

Then we repeated our analysis using the same procedure but replaced the “scene” time window with the “object” time window. The rationale for this control is that comparing the object cue to the immediately following fixation period should not reflect scene reinstatement, as the object and the reinstated scene rely on distinct neural representations. Accordingly, we did not expect a delay-related decrease in the reinstatement index. Consistent with this expectation, the analysis using the object – fixation similarity index – though also influenced by temporal autocorrelation – did not reveal any significant effect of session or delay in any ROI (all p > .059; see Table S9, S9.1).

Together, these control analyses provide converging evidence that our findings are not driven by global or non-specific signal changes. We believe that these control analyses strengthen our interpretation about delay-related decrease in scene-specific reinstatement index. 

(B) Do the recent items from day 1 vs. day 14 differ? If so, this could suggest something is different about the later scans (and if not, it would be reassuring). 

The recent items tested on day 1 and day14 do not differ (all p. > .323). This effect remains stable across all ROIs.

(b) For the category-based neural reinstatement: (1) This suffers from the same issue of correlations being performed within run. Again, to correct this the authors would need to restrict comparisons to only across runs (i.e., patterns from run 1 correlated with patterns for run 2 and so on). The authors in their response letter have indicated that because the patterns being correlated are not derived from events in close temporal proximity, they should not suffer from the issue of temporal autocorrelation. This is simply not true. For example, see the paper by Prince et al. (eLife 2022; on GLMsingle). This is not the main point of Prince et al.'s paper, but it includes a nice figure that shows that, using standard modelling approaches, the correlation between (same-run) patterns can be artificially elevated for lags as long as ~120 seconds (and can even be artificially reduced after that; Figure 5 from that paper) between events. This would affect many of the comparisons in the present paper. The cleanest way to proceed is to simply drop the within-run comparisons, which I believe the authors can do and yet they have not. Relatedly, in the response letter the authors say they are focusing mainly on the change over time for reinstatement at both levels including the gist-type reinstatement; however, this is not how it is discussed in the paper. They in fact are mainly relying on differences from zero, as children show some "above baseline" reinstatement while adults do not, but I believe there were no significant differences over time (i.e., the findings the authors said they would lean on primarily, as they are arguably the most comparable).  

We thank the reviewer for this important comment regarding the potential inflation of similarity values due to within-run comparisons.

To address the reviewer’s concern, we conducted an additional cross-run analysis for all correctly retrieved trials. The approach restricted comparisons to non-overlapping runs (run1run2, run2-run3, run1-run3). This analysis revealed robust gist-like reinstatement in children for remote Day 14 memories in the mPFC (p = .035) and vlPFC (p = .0007), in adults’ vlPFC remote Day 1 memories (p = .029), as well as in children and adults remote Day 1 memories in LOC (p < .02). A significant Session effect in both regions (mPFC: p = .026; vlPFC: p = .002) indicated increased reinstatement for long delay (Day 14) compared to short-delay and recent session (all p < .05). Given that the cross-run results largely replicate and reinforce the effects found previously with within-run, we believe that combining both sources of information is methodologically justified and statistically beneficial. Specifically, both approaches independently identified significant gist-like reinstatement in children’s mPFC and vlPFC (although within-run vlPFC effect (short delay: p = .038; long delay p = .047) did not survive multiple comparisons), particularly for remote memories. Including both withinrun and between-run comparisons increases the number of unique, non-repeated trial pairs, improving statistical power without introducing redundancy. While we acknowledge that same-run comparisons may be influenced by residual autocorrelation (as shown by Prince et al. 2022, eLife), we believe that our design mitigates this risk through consistency between within-run and cross-run results, long inter-trial intervals, and trial-wise estimation of activation. We have adjusted the manuscript, accordingly, reporting the combined analysis. We also report cross-run and within-run analysis separately in supplementary materials (Tables S12.1, S12.2, showing that they converge with the cross-run results and thus strengthen rather than dilute the findings. 

As suggested, we now explicitly highlight the change over time as the central finding. We observe a clear increase in gist-like reinstatement from recent to remote memories in children, particularly in mPFC and vlPFC. These effects based on combined within- and cross-run comparisons, are now clearly stated in the main results and interpreted in the discussion accordingly. 

(2) This analysis uses a different approach of comparing fixations to one another, rather than fixations to scenes. In their response letter and the revised paper, the authors do provide a bit of reasoning as to why this is the most sensible. However, it is still not clear to me whether this is really "reinstatement" which (in my mind) entails the re-evoking of a neural pattern initially engaged during perception. Rather, could this be a shared neural state that is category specific? 

We thank the reviewer for raising this important conceptual point about whether our findings reflect reinstatement in the classical sense — namely, the reactivation of perceptual neural patterns — or a shared, category-specific state.

While traditional definitions of reinstatement emphasize item-specific reactivation (e.g., Ritchey et al., 2013; Xiao et al., 2017) it is increasingly recognized that memory retrieval can also involve the reactivation of abstracted, generalized, or gist-like representations, especially as memories consolidate. Our analysis follows this view, aimed to capture how memory representations evolve over time, particularly in development.

Several studies support this broader notion of gist-like reinstatement. For instance, Chen et al. (2017) showed that while event-specific patterns were reinstated across the default mode network and medial temporal lobe, inter-subject recall similarity exceeded encodingretrieval similarity, suggesting transformation and abstraction beyond perceptual reinstatement. Zhuang et al. (2021) further showed that loss of neural distinctiveness in the

MTL over time predicted false memories, linking neural similarity to representational instability. This aligns with our finding that greater gist-like reinstatement is associated with lower memory accuracy.

Ye et al. (2020) discuss how memory representations are reshaped post-encoding — becoming more differentiated, integrated, or weakened depending on task goals and neural resources. While their work focuses on adults, our previous findings (Schommartz et al., 2023) suggest that children’s neural systems (the same sample) are structurally immature, making them more likely to rely on gist-based consolidation (see Fandakova et al., 2019). Adults, by contrast, may retain more item-specific traces.

Relatedly, St-Laurent & Buchsbaum (2019) show that with repeated encoding, neural memory representations become increasingly distinct from perception, suggesting that reinstatement need not mimic perception. We agree that reinstatement does not always reflect reactivation of low-level sensory patterns, particularly over long delays or in developing brains.

Finally, while we did not correlate retrieval patterns directly with perceptual encoding patterns, we assessed neural similarity among retrieved items within vs. between categories, based on non-repeated, independently sampled trials. This approach is intended to capture the structure and delay-related transformation of mnemonic representations, especially in terms of how they become more schematic or gist-like over time. Our findings align conceptually with the results of Kuhl et al. (2012), who used MVPA to show that older and newer visual memories can be simultaneously reactivated during retrieval, with greater reactivation of older memories interfering with retrieval accuracy for newer memories. Their work highlights how overlapping category-level representations in ventral temporal cortex can reflect competition among similar memories, even in the absence of item-specific cues. In our developmental context, we interpret the increased neural similarity among category members in children as possibly reflecting such representational overlap or competition, where generalized traces dominate over item-specific ones. This pattern may reflect a shift toward efficient but less precise retrieval, consistent with developmental constraints on memory specificity and consolidation.

In this context, we view our findings as evidence of memory trace reorganization — from differentiated, item-level representations toward more schematic, gist-like neural patterns (Sekeres et al., 2018), particularly in children. Our cross-run analyses further confirm that this is not an artifact of same-run correlations or low-level confounds. We have clarified this distinction and interpretation throughout the revised manuscript (see lines 144-158; 1163-1170).

In any case, I think additional information should be added to the text to clarify that this definition differs from others in the literature. The authors might also consider using some term other than reinstatement. Again (as I noted in my prior review), the finding of no category-level reinstatement in adults is surprising and confusing given prior work and likely has to do with the operationalization of "reinstatement" here. I was not quite sure about the explanation provided in the response letter, as category-level reinstatement is quite widespread in the brain for adults and is robust to differences in analytic procedures etc. 

We agree that our operationalization of "reinstatement" differs from more conventional uses of the term, which typically involve direct comparisons between encoding and retrieval phases, often with item-level specificity. As our analysis is based on similarity among retrieval-phase trials (fixation-based activation patterns) and focuses on within- versus between-category neural similarity, we agree that the term reinstatement may suggest a stronger encoding–retrieval mapping than we are claiming.

To avoid confusion and overstatement, we have revised the terminology throughout the manuscript: we now refer to our measure as “gist-like representations” rather than “gist-like reinstatement.” This change better reflects the nature of our analysis — namely, that we are capturing shared neural patterns among category-consistent memories that may reflect reorganized or abstracted traces, especially after delay and in development.

As the reviewer rightly points out, category-level reinstatement is well documented in adults (e.g., Kuhl & Chun, 2014; Tompary et al., 2020; Tompary & Davachi, 2017). The absence of such effects in our adult group may indeed reflect differences in study design, particularly our use of non-repeated, cross-trial comparisons based on fixation events. It may also reflect different consolidation strategies, with adults preserving more differentiated or item-specific representations, while children form more schematic or generalizable representations — a pattern consistent with our interpretation and supported by prior work (Fandakova et al., 2019; Sekeres et al., 2018) 

We have updated the relevant sections of the manuscript (Results, Discussion (particularly lines 1163- 1184), and Figure captions) to clarify this terminology shift and explicitly contrast our approach with more standard definitions of reinstatement. We hope this revision provides the needed conceptual clarity while preserving the integrity of our developmental findings.

(3) Also from a theoretical standpoint-I'm still a bit confused as to why gist-based reinstatement would involve reinstatement of the scene gist, rather than the object's location (on the screen) gist. Were the locations on the screen similar across scene backgrounds from the same category? It seems like a different way to define memory retrieval here would be to compare the neural patterns when cued to retrieve the same vs. similar (at the "gist" level) vs. different locations across object-scene pairs. This is somewhat related to a point from my review of the initial version of this manuscript, about how scene reinstatement is not necessary. The authors state that participants were instructed to reinstate the scene, but that does not mean they were actually doing it. The point that what is being measured via the reinstatement analyses is actually not necessary to perform the task should be discussed in more detail in the paper. 

We appreciate the reviewer’s thoughtful theoretical question regarding whether our measure of “gist-like representations” might reflect reinstatement of spatial (object-location) gist, rather than scene-level gist. We would like to clarify several key points about our task design and interpretation:

(1) Object locations were deliberately varied and context dependent.

In our stimulus set, each object was embedded in a rich scene context, and the locations were distributed across six distinct possible areas within each scene, with three possible object placements per location. These placements were manually selected to ensure realistic and context-sensitive positioning of objects within the scenes. Importantly, locations were not fixed across scenes within a given category. For example, objects placed in “forest” scenes could appear in different screen locations across different scene exemplars (e.g., one in the bottom-left side, another floating above). Therefore, the task did not introduce a consistent spatial schema across exemplars from the same scene category that could give rise to a “location gist.”

(2) Scene categories provided consistent high-level contextual information.

By contrast, the scene categories (e.g., farming, forest, indoor, etc.) provided semantically coherent and visually rich contextual backgrounds that participants could draw upon during retrieval. This was emphasized in the instruction phase, where participants were explicitly encouraged to recall the whole scene based on the stories they created during learning (not just the object or its position). While we acknowledge that we cannot directly verify the reinstated content, this instruction aligns with prior studies showing that scene and context reinstatement can occur even without direct task relevance (e.g., Kuhl & Chun, 2014; Ritchey et al., 2013).

(3) Our results are unlikely to reflect location-based reinstatement.

If participants had relied on a “location gist” strategy, we would have expected greater neural similarity across scenes with similar spatial layouts, regardless of category. However, our design avoids this confound by deliberately varying locations across exemplars within categories. Additionally, our categorical neural similarity measure contrasted within-category vs. between-category comparisons — making it sensitive to shared contextual or semantic structure, not simply shared screen positions.

Considering this, we believe that the neural similarity observed in the mPFC and vlPFC in children at long delay reflects the emergence of scene-level, gist-like representations, rather than low-level spatial regularities. Nevertheless, we now clarify this point in the manuscript and explicitly discuss the limitation that reinstatement of scene context was encouraged but not required for successful task performance.

Future studies could dissociate spatial and contextual components of reinstatement more directly by using controlled spatial overlap or explicit location recall conditions. However, given the current task structure, location-based generalization is unlikely to account for the category-level similarity patterns we observe.

(2) Inspired by another reviewer's comment, it is unclear to me the extent to which age group differences can be attributed to differences in age/development versus memory strength. I liked the other reviewer's suggestions about how to identify and control for differences in memory strength, which I don't think the authors actually did in the revision. They instead showed evidence that memory strength does seem to be lower in children, which indicates this is an interpretive confound. For example, I liked the reviewer's suggestion of performing analyses on subsets of participants who were actually matched in initial learning/memory performance would have been very informative. As it is, the authors didn't really control for memory strength adequately in my opinion, and as such their conclusions about children vs. adults could have been reframed as people with weak vs. strong memories. This is obviously a big drawback given what the authors want to conclude. Relatedly, I'm not sure the DDM was incorporated as the reviewer was suggesting; at minimum I think the authors need to do more work in the paper to explain what this means and why it is relevant. (I understand putting it in the supplement rather

than the main paper, but I still wanted to know more about what it added from an interpretive perspective.) 

We appreciate the reviewer’s thoughtful concerns regarding potential confounding effects of memory strength on the observed age group differences. This is indeed a critical issue when interpreting developmental findings.

While we agree that memory strength differs between children and adults — and our own DDM-based analysis confirms this, mirroring differences observed in accuracy — we would like to emphasize that these differences are not incidental but rather reflect developmental changes in the underlying memory system. Given the known maturation of both structural and functional memory-related brain regions, particularly the hippocampus and prefrontal cortex, we believe it would be theoretically inappropriate to control for memory strength entirely, as doing so would remove variance that is central to the age-related neural effects we aim to understand.

To address the reviewer's concern empirically, we conducted an additional control analysis in which we subsampled children to include only those who reached learning criterion after two cycles (N = 28 out of 49 children, see Table S1.1, S1.2, Figure S1, Table S9.1), thereby selecting a high-performing subgroup. Importantly, this subsample replicated behavioral and neural results to the full group. This further suggests that the observed age group differences are not merely driven by differences in memory strength.

As abovementioned, the results of the DDM support our behavioral findings, showing that children have lower drift rates for evidence accumulation, consistent with weaker or less accessible memory representations. While these results are reported in the Supplementary Materials (section S2.1, Figure S2, Table S2), we agree that their interpretive relevance should be more clearly explained in the main text. We have therefore updated the Discussion section to explicitly state how the DDM results provide converging evidence for our interpretation that developmental differences in memory quality — not merely strategy or task performance — underlie the observed neural differences (see lines 904-926).

In sum, we view memory strength not as a confound to be removed, but as a meaningful and theoretically relevant factor in understanding the emergence of gist-like representations in children. We have clarified this interpretive stance in the revised manuscript and now discuss the role of memory strength more explicitly in the Discussion.

(3) Some of the univariate results reporting is a bit strange, as they are relying upon differences between retrieval of 1- vs. 14-day memories in terms of the recent vs. remote difference, and yet don't report whether the regions are differently active for recent and remote retrieval. For example in Figure 3A, neither anterior nor posterior hippocampus seem to be differentially active for recent vs. remote memories for either age group (i.e., all data is around 0). Precuneus also interestingly seems to show numerically recent>remote (values mostly negative), whereas most other regions show the opposite. This difference from zero (in either direction) or lack thereof seems important to the message. In response to this comment on the original manuscript, the authors seem to have confirmed that hippocampal activity was greater during retrieval than implicit baseline. But this was not really my question - I was asking whether hippocampus is (and other ROIs in this same figure are) differently engaged for recent vs. remote memories.

We thank the reviewer for bringing up this important point. Our previous analysis showed that both anterior and posterior regions of the hippocampus, anterior parahippocampal gyrus and precuneus exhibited significant activation from zero in children and adults for correctly remembered items (see Fig. S2, Table S7 in Supplementary Materials). Based on your suggestion, our additional analysis showed: 

(i) The linear mixed-effects model for correctly remembered items showed no significant interaction effects (group x session x memory age (recent, remote)) for the anterior hippocampus (all p > .146; see Table S7.1).

(ii) For the posterior hippocampus, we observed a significant main effect of group (F(1,85),   = 5.62, p = .038), showing significantly lower activation in children compared to adults (b = .03, t = -2.34, p = .021). No other main or interaction effects were significant (all p > .08; see Table S7.1).

(iii) For the anterior PHG, that also showed no significant remote > recent difference, the model showed that there was indeed no difference between remote and recent items across age groups and delays (all p > .194; Table S7.1). 

Moreover, when comparing recent and remote hippocampal activation directly, there were no significant differences in either group (all FDR-adjusted p > .116; Table S7.2), supporting the conclusion that hippocampal involvement was stable across delays for successfully retrieved items. 

In contrast, analysis of unsuccessfully remembered items showed that hippocampal activation was not significantly different from zero in either group (all FDR-adjusted p > .052; Fig. S2.1, Table S7.1), indicating that hippocampal engagement was specific to successful memory retrieval.

To formally test whether hippocampal activation differs between remembered and forgotten items, we ran a linear mixed-effects model with Group, Memory Success (remembered vs. forgotten), and ROI (anterior vs. posterior hippocampus) as fixed effects. This model revealed a robust main effect of memory success (F(1,1198) = 128.27, p < .001), showing that hippocampal activity was significantly higher for remembered compared to forgotten items (b = .06, t(1207) = 11.29, p < .001; Table S7.3). 

As the reviewer noted, precuneus activation was numerically higher for recent vs. remote items, and this was confirmed in our analysis. While both recent and remote retrieval elicited significantly above-zero activation in the precuneus (Table S7.2), activation for recent items was significantly higher than for remote items, consistent across both age groups.

Taken together, these analyses support the conclusion that hippocampal involvement in successful retrieval is sustained across delays, while other ROIs such as the precuneus may show greater engagement for more recent memories. We have now updated the manuscript text ( lines 370-390) and supplementary materials to reflect these findings more clearly, as well as to clarify the distinction between activation relative to baseline and memory-agerelated modulation.

(4) Related to point 3, the claims about hippocampus with respect to multiple trace theory feel very unsupported by the data. I believe the authors want to conclude that children's memory retrieval shows reliance on hippocampus irrespective of delay, presumably because this is a detailed memory task. However the authors have not really shown this; all they have shown is that hippocampal involvement (whatever it is) does not vary by delay. But we do not have compelling evidence that the hippocampus is involved in this task at all. That hippocampus is more active during retrieval than implicit baseline is a very low bar and does not necessarily indicate a role in memory retrieval. If the authors want to make this claim, more data are needed (e.g., showing that hippocampal activity during retrieval is higher when the upcoming memory retrieval is successful vs. unsuccessful). In the absence of this, I think all the claims about multiple trace theory supporting retrieval similarly across delays and that this is operational in children are inappropriate and should be removed. 

We thank the reviewer for pointing this out. We agree that additional analysis of hippocampal activity during successful and unsuccessful memory retrieval is warranted. This will provide stronger support for our claim that strong, detailed memories during retrieval rely on the hippocampus in both children and adults. Our previously presented results on the remote > recent univariate signal difference in the hippocampus (p. 14-18; lines 433-376, Fig. 3A) show that this difference does not vary between children and adults, or between Day 1 and Day 14. Our further analysis showed that both anterior and posterior regions of the hippocampus exhibited significant activation from zero in children and adults for correctly remembered items (see Fig. S2, Table S7 in Supplementary Materials). Based on your suggestion, our recent additional analysis showed:

(i) For forgotten items, we did not observe any activation significantly higher than zero in either the anterior or posterior hippocampus for recent and remote memory on Day 1 and Day 14 in either age group (all p > .052 FDR corrected; see Table S7.1, Fig. S2.1).

(ii) After establishing no difference between recent and remote activation across and between sessions (Day 1, Day 14), we conducted another linear mixed-effects model with group x memory success (remembered, forgotten) x region (anterior hippocampus, posterior hippocampus), with subject as a random effect. The model showed no significant effects for the memory success x region interaction (F = 1.12(1,1198), p = .289) and no significant group x memory success x region interaction (F = .017(1,1198), p = .895). However, we observed a significant main effect of memory success (F = 128.27(1,1198), p < .001), indicating significantly higher hippocampal activation for remembered compared to forgotten items (b = .06, t = 11.29, p <.001; see Table S7.3).

(iii) Considering the comparatively low number of incorrect trials for recent items in the adult group, we reran this analysis only for remote items. Similarly, the model showed no significant effects for the memory success x region interaction (F = .72(1,555), p = .398) and no significant group x memory success x region interaction (F = .14(1,555), p = .705). However, we observed a significant main effect of memory success (F = 68.03(1,555), p < .001), indicating significantly higher hippocampal activation for remote remembered compared to forgotten items (b = .07, t = 8.20, p <.001; see Table S7.3).

Taken together, our results indicate that significant hippocampal activation was observed only for correctly remembered items in both children and adults, regardless of memory age and session. For forgotten items, we did not observe any significant hippocampal activation in either group or delay. Moreover, hippocampal activation was significantly higher for remembered compared to forgotten memories. This evidence supports our conclusions regarding the Multiple Trace and Trace Transformation Theories, suggesting that the hippocampus supports retrieval similarly across delays, and provides novel evidence that this process is operational in both children and adults. This aligns also with Contextual Bindings Theory, as well as empirical evidence by Sekeres, Winokur, & Moscovitch (2018), among others. We have added this information to the manuscript.

(5) There are still not enough methodological details in the main paper to make sense of the results. Some of these problems were addressed in the revision but others remain. For example, a couple of things that were unclear: that initially learned locations were split, where half were tested again at day 1 and the other half at day 14; what specific criterion was used to determine to pick the 'well-learned' associations that were used for comparisons at different delay periods (object-scene pairs that participants remembered accurately in the last repetition of learning? Or across all of learning?). 

We thank the reviewer for pointing this out. The initially learned object-scene associations on Day 0 were split in two halves based on  their categories before the testing. Specifically, half of the pairs from the first set and half of the pairs from the second set of 30 object-scene associations were used to create the set 30 remote pair for Day 1 testing. A similar procedure was repeated for the remaining pairs to create a set of remote object-scene associations for Day 14 retrieval. We tried to equally distribute the categories of pairs between the testing sets. We added this information to the methods section of the manuscript (see p. 47, lines 12371243). In addition, the sets of association for delay test on Day 1 and Day 14 were not based on their learning accuracy. Of note, the analysis of variance revealed that there was no difference in learning accuracy between the two sets created for delay tests in either age group (children: p = .23; adults  p = .06). These results indicate that the sets were comprised of items learned with comparable accuracy in both age groups. 

(6) In still find the revised Introduction a bit unclear. I appreciated the added descriptions of different theories of consolidation, though the order of presented points is still a bit hard to follow. Some of the predictions I also find a bit confusing as laid out in the introduction. (1) As noted in the paper multiple trace theory predicts that hippocampal involvement will remain high provided memories retained are sufficiently high detail. The authors however also predict that children will rely more on gist (than detailed) memories than adults, which would seem to imply (combined with the MTT idea) that they should show reduced hippocampal involvement over time (while in adults, it should remain high). However, the authors' actual prediction is that hippocampus will show stable involvement over time in both kids and adults. I'm having a hard time reconciling these points. (2) With respect to the extraction of gist in children, I was confused by the link to Fuzzy Trace Theory given the children in the present study are a bit young to be showing the kind of gist extraction shown in the Brainerd & Reyna data. Would 5-7 year olds not be more likely to show reliance on verbatim traces under that framework? Also from a phrasing perspective, I was confused about whether gist-like information was something different from just gist in this sentence: "children may be more inclined to extract gist information at the expense of detailed or gist-like information." (p. 8) - is this a typo? 

We thank the reviewer for this thoughtful observation. 

Our hypothesis of stable hippocampal engagement over time was primarily based on Contextual Binding Theory (Yonelinas et al., 2019), and the MTT, supported by the evidence provided by Sekeres et al., 2018, which posits that the hippocampus continues to support retrieval when contextual information is preserved, even for older, consolidated memories. Given that our object-location associations were repeatedly encoded and tied to specific scene contexts, we believe that retrieval success for both recent and remote memories likely involved contextual reinstatement, leading to sustained hippocampal activity. Also in accordance with the MTT and related TTT, different memory representations may coexist, including detailed and gist-like memories. Therefore, we suggest that children may not rely on highly detailed item-specific memory, but rather on sufficiently contextualized schematic traces, which still engage the hippocampus. This distinction is now made clearer in the Introduction (see lines 223-236).

We appreciate the reviewer’s point regarding Fuzzy Trace Theory (Brainerd & Reyna, 2002). Indeed, in classic FTT, young children are thought to rely more on verbatim traces due to immature gist extraction mechanisms (primarily from verbal material). However, we use the term “gist-like representations” to refer to schematic or category-level retrieval that emerges through structured, repeated learning (as in our task). This form of abstraction may not require full semantic gist extraction in the FTT sense but may instead reflect consolidation-driven convergence onto shared category-level representations — especially when strategic resources are limited. We now clarify this distinction and revise the ambiguous sentence with typo (“at the expense of detailed or gist-like information”) to better reflect our intended meaning (see p.8).

(7) For the PLSC, if I understand this correctly, the profiles were defined for showing associations with behaviour across age groups. (1) As such, is it not "double dipping" to then show that there is an association between brain profile and behaviour-must this not be true by definition? If I am mistaken, it might be helpful to clarify this in the paper. (2) In addition, I believe for the univariate and scene-specific reinstatement analyses these profiles were defined across both age groups. I assume this doesn't allow for separate definition of profiles across the two group (i.e., a kind of "interaction"). If this is the case, it makes sense that there would not be big age differences... the profiles were defined for showing an association across all subjects. If the authors wanted to identify distinct profiles in children and adults they may need to run another analysis. 

We thank the reviewer for this thoughtful comment. 

(1) We agree that showing the correlation between the latent variable and behavior may be redundant, as the relationship is already embedded in the PLSC solution and quantified by the explained variance. Our intention was merely to visualize the strength of this relationship. In hindsight, we agree that this could be misinterpreted, and we have removed the additional correlation figure from the manuscript.

We also see the reviewer’s point that, given the shared latent profile across groups, it is expected that the strength of the brain-behavior relationship does not differ between age groups. Instead, to investigate group differences more appropriately, we examined whether children and adults differed in their expression of the shared latent variable (i.e., brain scores). This analysis revealed that children showed significantly lower brain scores than adults both in short delay, t(83) = -4.227, p = .0001, and long delay, t(74) = -5.653, p < .001, suggesting that while the brain-behavior profile is shared, its expression varies by group. We have added this clarification to the Results section (p. 19-20) of the revised manuscript. 

(2) Regarding the second point, we agree with the reviewer that defining the PLS profiles across both age groups inherently limits the ability to detect group-specific association, as the resulting latent variables represent shared pattern across the full sample. To address this, we conducted additional PLS analyses separately within each age group to examine whether distinct neural upregulation profiles (remote > recent) emerge for short and long delay conditions.

These within-group analyses, however, were based on smaller subsamples, which reduced statistical power, especially when using bootstrapping to assess the stability of the profiles. For the short delay, although some regions reached significance, the overall latent variables did not reach conventional thresholds for stability (all p > .069), indicating that the profiles were not robust. This suggests that within-group PLS analyses may be underpowered to detect subtle effects, particularly when modelling neural upregulation (remote > recent), which may be inherently small.

Nonetheless, when we exploratively applied PLSC separately within each group using recent and remote activity levels against the implicit baseline (rather than the contrast remote > recent) and its relation to memory performance, we observed significant and stable latent variables in both children and adults. This implies that such contrasts (vs. baseline) may be more sensitive and better suited to detect meaningful brain–behavior relationships within age groups. We have added this clarification to the Results sections of the manuscript to highlight the limitations of within-group contrasts for neural upregulation. 

Author response image 1.

(3) Also, as for differences between short delay brain profile and long delay brain profile for the scene-specific reinstatement - there are 2 regions that become significant at long delay that were not significant at a short delay (PC, and CE). However, given there are ceiling effects in behaviour at the short but not long delay, it's unclear if this is a meaningful difference or just a difference in sensitivity. Is there a way to test whether the profiles are statistically different from one another?

We thank the reviewer for this comment. To better illustrate differential profiles also for high memory accuracy after immediate delay (30 minutes delay), we added the immediate (30 minutes delay) condition as a third reference point, given the availability of scene-specific reinstatement data at this time point. Interestingly, the immediate reinstatement profile revealed a different set of significant regions, with distinct expression patterns compared to both the short and long delay conditions. This supports the view that scene-specific reinstatement is not static but dynamically reorganized over time.

Regarding the ceiling effect at short delay, we acknowledge this as a potential limitation. However, we note that our primary analyses were conducted across both age groups combined, and not solely within high-performing individuals. As such, the grouping may mitigate concerns that ceiling-level performance in a subset of participants unduly influenced the overall reinstatement profile. Moreover, we observed variation in neural reinstatement despite ceiling-level behavior, suggesting that the neural signal retains sensitivity to consolidation-related processes even when behavioral accuracy is near-perfect.

While we agree that formal statistical comparisons of reinstatement profiles across delays (e.g., using representational profile similarity or interaction tests) could be an informative direction, we feel that this goes beyond the scope of the current manuscript. 

(4) As I mentioned above, it also was not ideal in my opinion that all regions were included for the scene-specific reinstatement due to the authors' inability to have an appropriate baseline and therefore define above-chance reinstatement. It makes these findings really challenging to compare with the gist reinstatement ones. 

We appreciate the reviewer’s comment and agree that the lack of a clearly defined baseline for scene-specific reinstatement limits our ability to determine whether these values reflect above-chance reinstatement. However, we would like to clarify that we do not directly compare the magnitude of scene-specific reinstatement to that of gist-like reinstatement in our analyses or interpretations. These two analyses serve complementary purposes: the scenespecific analysis captures trial-unique similarity (within-item reinstatement), while the gistlike analysis captures category-level representational structure (across items). Because they differ not only in baseline assumptions but also in analytical scope and theoretical interpretation, our goal was not to compare them directly, but rather to explore distinct but co-existing representational formats that may evolve differently across development and delay.

(8) I would encourage the authors to be specific about whether they are measuring/talking about memory representations versus reinstatement, unless they think these are the same thing (in which case some explanation as to why would be helpful). For example, especially under the Fuzzy Trace framework, couldn't someone maintain both verbatim and gist traces of a memory yet rely more on one when making a memory decision? 

We thank the reviewer for pointing out the importance of conceptual clarity when referring to memory representations versus reinstatement. We agree that these are distinct but related concepts: in our framework, memory representations refer to the neural content stored as a result of encoding and consolidation, whereas reinstatement refers to the reactivation of those representations during retrieval. Thus, reinstatement serves as a proxy for the underlying memory representation — it is how we measure or infer the nature (e.g., specificity, abstraction) of the stored content.

Under Fuzzy Trace Theory, it is indeed possible for both verbatim and gist representations to coexist. Our interpretation is not that children lack verbatim traces, but rather that they are more likely to rely on schematic or gist-like representations during retrieval, especially after a delay. Our use of neural pattern similarity (reinstatement) reflects which type of representation is being accessed, not necessarily which traces exist in parallel.

To avoid ambiguity, we have revised the manuscript to more explicitly distinguish between reinstatement (neural reactivation) and the representational format (verbatim vs. gist-like), especially in the framing of our hypotheses and interpretation of age group differences.

(9) With respect to the learning criteria - it is misleading to say that "children needed between two to four learning-retrieval cycles to reach the criterion of 83% correct responses" (p. 9). Four was the maximum, and looking at the Figure 1C data it appears as though there were at least a few children who did not meet the 83% minimum. I believe they were included in the analysis anyway? Please clarify. Was there any minimum imposed for inclusion?

We thank the reviewer for pointing this out. As stated in Methods Section (p. 50, lines 13261338) “These cycles ranged from a minimum of two to a maximum of four.<…> The cycles ended when participants provided correct responses to 83% of the trials or after the fourth cycle was reached.” We have corrected the corresponding wording in the Results section (line 286-289) to reflect this more accurately. Indeed, five children did not reach the 83% criterion but achieved final performance between 70 and 80% after the fourth learning cycle. These participants were included in this analysis for two main reasons:

(1) The 83% threshold was established during piloting as a guideline for how many learningretrieval cycles to allow, not a strict learning criterion. It served to standardize task continuation, rather than to exclude participants post hoc.

(2) The performance of these five children was still well above chance level (33%), indicating meaningful learning. Excluding them would have biased the sample toward higherperforming children and reduced the ecological validity of our findings. Including them ensures a more representative view of children’s performance under extended learning conditions.

(10) For the gist-like reinstatement PLSC analysis, results are really similar a short and long delays and yet some of the text seems to implying specificity to the long delay. One is a trend and one is significant (p. 31), but surely these two associations would not be statistically different from one another?  

We agree with the reviewer that the associations at short and long delays appeared similar. While a formal comparison (e.g., using a Z-test for dependent correlations) would typically be warranted, in the reanalyzed dataset only the long delay profile remains statistically significant, which limits the interpretability of such a comparison. 

(11) As a general comment, I had a hard time tying all of the (many) results together. For example adults show more mature neocortical consolidation-related engagement, which the authors say is going to create more durable detailed memories, but under multiple trace theory we would generally think of neocortical representations as providing more schematic information. If the authors could try to make more connections across the different neural analyses, as well as tie the neural findings in more closely with the behaviour & back to the theoretical frameworks, that would be really helpful.  

We thank the reviewer for this valuable suggestion. We have revised the discussion section to more clearly link the behavioral and neural findings and to interpret them in light of existing consolidation theories for better clarity. 

Reviewer #2 (Public Review): 

Schommartz et al. present a manuscript characterizing neural signatures of reinstatement during cued retrieval of middle-aged children compared to adults. The authors utilize a paradigm where participants learn the spatial location of semantically related item-scene memoranda which they retrieve after short or long delays. The paradigm is especially strong as the authors include novel memoranda at each delayed time point to make comparisons across new and old learning. In brief, the authors find that children show more forgetting than adults, and adults show greater engagement of cortical networks after longer delays as well as stronger item-specific reinstatement. Interestingly, children show more category-based reinstatement, however, evidence supports that this marker may be maladaptive for retrieving episodic details. The question is extremely timely both given the boom in neurocognitive research on the neural development of memory, and the dearth of research on consolidation in this age group. Also, the results provide novel insights into why consolidation processes may be disrupted in children. 

We thank the reviewer for the positive evaluation.

Comments on the revised version: 

I carefully reviewed not only the responses to my own reviews as well as those raised by the other reviewers. While they addressed some of the concerns raised in the process, I think many substantive concerns remain. 

Regarding Reviewer 1: 

The authors point that the retrieval procedure is the same over time and similarly influenced by temporal autocorrelations, which makes their analysis okay. However, there is a fundamental problem as to whether they are actually measuring reinstatement or they are only measuring differences in temporal autocorrelation (or some non-linear combination of both). The authors further argue that the stimuli are being processed more memory wise rather than perception wise, however, I think there is no evidence for that and that perception-memory processes should be considered on a continuum rather than as discrete processes. Thus, I agree with reviewer 1 that these analyses should be removed. 

We thank the reviewer for raising this important question. We would like to clarify a few key points regarding temporal autocorrelation and reinstatement.

During the fixation window, participants were instructed to reinstate the scene and location associated with the cued object from memory. This task was familiar to them, as they had been trained in retrieving locations within scenes. Our analysis aims to compare the neural representations during this retrieval phase with those when participants view the scene, in order to assess how these representations change in similarity over time, as memories become less precise.

We acknowledge that temporal proximity can lead to temporal autocorrelation. However, evidence suggests that temporal autocorrelation is consistent and stable across conditions (Gautama & Van Hulle, 2004; Woolrich et al., 2004). Shinn & Lagalwar (2021)further demonstrated that temporal autocorrelation is highly reliable at both the subject and regional levels. Given that we analyze regions of interest (ROIs) separately, potential spatial variability in temporal autocorrelation is not a major concern.

No difference between item-specific reinstatement for recent items on day 1 and day 14 (which were merged) for further delay-related comparison also suggests that the reinstatement measure was stable for recent items even sampled at two different testing days. 

Importantly, we interpret the relative change in the reinstatement index rather than its absolute value.

In addition, when we conducted the same analysis for incorrectly retrieved memories, we did not observe any delay-related decline in reinstatement (see p. 25, lines 623-627). This suggests that the delay-related changes in reinstatement are specific to correctly retrieved memories. 

Finally, our control analysis examining reinstatement between object and fixation time points (as suggested by Reviewer 1) revealed no delay-related effects in any ROI (see p.24, lines 605-612), further highlighting the specificity of the observed delay-related change in item reinstatement.

We emphasize that temporal autocorrelation should be similar across all retrieval delays due to the identical task design and structure. Therefore, any observed decrease in reinstatement with increasing delay likely reflects a genuine change in the reinstatement index, rather than differences in temporal autocorrelation. Since our analysis includes only correctly retrieved items, and there is no perceptual input during the fixation window, this process is inherently memory-based, relying on mnemonic retrieval rather than sensory processing.

We respectfully disagree with the reviewer's assertion that retrieval during the fixation period cannot be considered more memory-driven than perception-driven. At this time point, participants had no access to actual images of the scene, making it necessary for them to rely on mnemonic retrieval. The object cue likely triggered pattern completion for the learned object-scene association, forming a unique memory if remembered correctly(Horner & Burgess, 2013). This process is inherently mnemonic, as it is based on reconstructing the original neural representation of the scene (Kuhl et al., 2012; Staresina et al., 2013).

While perception and memory processes can indeed be viewed as a continuum, some cognitive processes are predominantly memory-based, involving reconstruction rather than reproduction of previous experiences (Bartlett, 1932; Ranganath & Ritchey, 2012). In our task, although the retrieved material is based on previously encoded visual information, the process of recalling this information during the fixation period is fundamentally mnemonic, as it does not involve visual input. Our findings indicate that the similarity between memorybased representations and those observed during actual perception decreases over time, suggesting a relative change in the quality of the representations. However, this does not imply that detailed representations disappear; they may still be robust enough to support correct memory recall. Previous studies examining encoding-retrieval similarity have shown similar findings(Pacheco Estefan et al., 2019; Ritchey et al., 2013).

We do not claim that perception and memory processes are entirely discrete, nor do we suggest that only perception is involved when participants see the scene. Viewing the scene indeed involves recognition processes, updating retrieved representations from the fixation period, and potentially completing missing or unclear information. This integrative process demonstrates the interrelation of perception and memory, especially in complex tasks like the one we employed.

In conclusion, our task design and analysis support the interpretation that the fixation period is primarily characterized by mnemonic retrieval, facilitated by cue-triggered pattern completion, rather than perceptual processing. We believe this approach aligns with the current understanding of memory retrieval processes as supported by the existing literature.

The authors seem to have a design that would allow for across run comparisons, however, they did not include these additional analyses. 

Thank you for pointing this out. We ran as additional cross-run comparison. This results and further proceeding are reported in the comment for reviewer 1. 

To address the reviewer’s concern, we conducted an additional cross-run analysis for all correctly retrieved trials. The approach restricted comparisons to non-overlapping runs (run1run2, run2-run3, run1-run3). This analysis revealed robust gist-like reinstatement in children for remote Day 14 memories in the mPFC (p = .035) and vlPFC (p = .0007), in adults’ vlPFC remote Day 1 memories (p = .029), as well as in children and adults remote Day 1 memories in LOC (p < .02). A significant Session effect in both regions (mPFC: p = .026; vlPFC: p = .002) indicated increased reinstatement for long delay (Day 14) compared to short-delay and recent session (all p < .05). Given that the cross-run results largely replicate and reinforce the effects found previously with within-run, we believe that combining both sources of information is methodologically justified and statistically beneficial. Specifically, both approaches independently identified significant gist-like reinstatement in children’s mPFC and vlPFC (although within-run vlPFC effect (short delay: p = .038; long delay p = .047) did not survive multiple comparisons), particularly for remote memories. Including both withinrun and between-run comparisons increases the number of unique, non-repeated trial pairs, improving statistical power without introducing redundancy. While we acknowledge that same-run comparisons may be influenced by residual autocorrelation(Prince et al., 2022), we believe that our design mitigates this risk through consistency between within-run and crossrun results, long inter-trial intervals, and trial-wise estimation of activation. We have adjusted the manuscript, accordingly, reporting the combined analysis. We also report cross-run and within-run analysis separately in supplementary materials (Tables S12.1, S12.2, showing that they converge with the cross-run results and thus strengthen rather than dilute the findings. 

As suggested, we now explicitly highlight the change over time as the central finding. We observe a clear increase in gist-like reinstatement from recent to remote memories in children, particularly in mPFC and vlPFC. These effects based on combined within- and cross-run comparisons, are now clearly stated in the main results and interpreted in the discussion accordingly. 

(1) The authors did not satisfy my concerns about different amounts of re-exposures to stimuli as a function of age, which introduces a serious confound in the interpretation of the neural data. 

(2) Regarding Reviewer 1's point about different number of trials being entered into analysis, I think a more formal test of sub-sampling the adult trials is warranted. 

(1) We thank the reviewer for pointing this out. Overall, children needed 2 to 4 learning cycles to improve their performance and reach the learning criteria, compared to 2 learning cycles in adults. To address the different amounts of re-exposure to stimuli between the age groups, we subsampled the child group to only those children who reached the learning criteria after 2 learning cycles. For this purpose, we excluded 21 children from the analysis who needed 3 or 4 learning cycles. This resulted in 39 young adults and 28 children being included in the subsequent analysis. 

(i) We reran the behavioral analysis with the subsampled dataset (see Supplementary Materials,  Table S1.1, Fig. S1, Table S1.2). This analysis replicated the previous findings of less robust memory consolidation in children across all time delays. 

(ii) We reran the univariate analysis (see in Supplementary Materials, Table S9.1). This analysis also replicated fully the previous findings. This indicates that the inclusion of child participants with greater material exposure during learning in the analysis of neural retrieval patterns did not affect the group differences in univariate neural results. 

These subsampled results demonstrated that the amount of re-exposure to stimuli during encoding does not affect consolidation-related changes in memory retrieval at the behavioral and neural levels in children and adults across all time delays. We have added this information to the manuscript (line 343-348, 420-425). 

(2) We appreciate Reviewer 1's suggestion to perform a formal test by sub-sampling the adult trials to match the number of trials in the child group. However, we believe that this approach may not be optimal for the following reasons:

(i) Loss of Statistical Power: Sub-sampling the adult trials would result in a reduced sample size, potentially leading to a significant loss of statistical power and the ability to detect meaningful effects, particularly in a context where the adult group is intended to serve as a robust control or comparison group.

(ii) Introducing sub-sampling could introduce variability that complicates the interpretation of results, particularly if the trial sub-sampling process does not fully capture the variability inherent in the original adult data.

(iii) Robustness of Existing Findings: We have already addressed potential concerns about unequal trial numbers by conducting analyses that control for the number of learning cycles, as detailed in our supplementary materials. These analyses have shown that the observed effects are consistent, suggesting that the differences in trial numbers do not critically influence our findings.

Given these considerations, we hope the reviewer understands our rationale and agrees that the current analysis is robust and appropriate for addressing the research questions.

I also still fundamentally disagree with the use of global signals when comparing children to adults, and think this could very much skew the results. 

We thank the reviewer for raising this important issue. To address this concern comprehensively, we have taken the following steps:

(1) Overview of the literature support for global signal regression (GSR). A growing body of methodological and empirical research supports the inclusion of global signal repression as part of best practice denoising pipelines, particularly when analyzing pediatric fMRI data. Studies such as (Ciric et al., 2017; Parkes et al., 2018; J. D. Power et al., 2012, 2014; Power et al., 2012), and (Thompson et al., 2016) show that  GSR improves motion-related artifact removal. Critically, pediatric-specific studies (Disselhoff et al., 2025; Graff et al., 2022) conclude that pipelines including GSR are most effective for signal recovery and artifact removal in younger children. Graff et al. (2021) demonstrated that among various pipelines, GSR yielded the best noise reduction in 4–8-year-olds. Additionally, (Li et al., 2019; Qing et al., 2015) emphasized that GSR reduces artifactual variance without distorting the spatial structure of neural signals. (Ofoghi et al., 2021)demonstrated that global signal regression helps mitigate non-neuronal noise sources, including respiration, cardiac activity, motion, vasodilation, and scanner-related artifacts. Based on this and other recent findings, we consider GSR particularly beneficial for denoising paediatric  fMRI data in our study.

(2) Empirical comparison of pipelines with and without GSR. We re-run the entire first-level univariate analysis using the pipeline that excluded the global signal regression. The resulting activation maps (see Supplementary Figure S3.2, S4.2, S5.2, S9.2) differed notably from the original pipeline. Specifically, group differences in cortical regions such as mPFC, cerebellum, and posterior PHG no longer reached significance, and the overall pattern of results appeared noisier. 

(3) Evaluation of the pipeline differences. To further evaluate the impact of GSR, we conducted the following analyses:

(a) Global signal is stable across groups and sessions. A linear mixed-effects model showed no significant main effects or interactions involving group or session on the global signal (F-values < 2.62, p > .11), suggesting that the global signal was not group- or session-dependent in our sample. 

(b) Noise Reduction Assessment via Contrast Variability. We compared the variability (standard deviation and IQR) of contrast estimates across pipelines. Both SD (b = .070, p < .001) and IQR (b = .087, p < .001) were significantly reduced in the GSR pipeline, especially in children (p < .001) compared to adults (p = .048). This suggests that GSR reduces inter-subject variability in children, likely reflecting improved signal quality.

(c) Residual Variability After Regressing Global Signal. We regressed out global signal post hoc from both pipelines and compared the residual variance. Residual standard deviation was significantly lower for the GSR pipeline (F = 199, p < .001), with no interaction with session or group, further indicating that GSR stabilizes the signal and attenuates non-neuronal variability.

Conclusion

In summary, while we understand the reviewer’s concern, we believe the empirical and theoretical support for GSR, especially in pediatric samples, justifies its use in our study. Nonetheless, to ensure full transparency, we provide full results from both pipelines in the Supplementary Materials and have clarified our reasoning in the revised manuscript.

Reviewer #1 (Recommendations For The Authors): 

(1) Some figures are still missing descriptions of what everything on the graph means; please clarify in captions. 

We thank the reviewer for pointing this out. We undertook the necessary adjustments in the graph annotations. 

(2) The authors conclude they showed evidence of neural reorganization of memory representations in children (p. 41). But the gist is not greater in children than adults, and also does not differ over time-so, I was confused about what this claim was based on? 

We thank the reviewer for raising this question. Our results on gist-like reinstatements suggest that gist-like reinstatement was significantly higher in children compared to adults in the mPFC in addition to the child gist-like reinstatement indices being significantly higher than zero (see p.27-28). These results support our claim on neural reorganization of memory represenations in children. We hope this clarifies the issue. 

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https://doi.org/10.1038/s41562-021-01188-4

eLife Assessment

This study presents fundamental insights into overcoming resistance in hormone receptor-positive breast cancer by demonstrating that sustained CDK4/6 inhibitor treatment, either alone or in combination with CDK2 inhibitors, significantly suppresses the growth of drug-resistant cancer cells. The findings are supported by compelling evidence from both in vitro cell line experiments and in vivo mouse models, highlighting the therapeutic potential of maintaining CDK4/6 inhibitors beyond disease progression. Additionally, the identification of cyclin E overexpression as a key driver of resistance offers a target that will be of value for future therapeutic strategies, potentially improving outcomes for patients with advanced breast cancer.

Reviewer #1 (Public review):

Summary:

In the research manuscript submitted to eLife (Manuscript ID eLife-RP-RA-2024-104545) titled "Therapeutic benefits of maintaining CDK4/6 inhibitors and incorporating CDK2 inhibitors beyond progression in breast cancer" authors identified 1) CDK4/6i treatment attenuates the growth of drug-resistant cell by prolongation of G1 phase; 2) CDK4/6i treatment results in an ineffective Rb inactivation pathways and suppress the growth of drug-resistant tumors; 3) Addition of endocrine therapy augments the efficacy of CDK4/6i maintenance; 4) Addition of CDK2i with CDK4/6 treatment as second-line treatment can suppress the growth of resistant cell; 5) finally role of cyclin E as key driver of resistance to CDK4/6 and CDK2 inhibition.

Strengths:

To prove authors complicated proposal, authors employed orchestration of several kinds of live cell markers, timed in situ hybridization, IF and Immono-bloting. The authors strongly recognize the resistance of CDK4/6 + ET therapy and demonstrated how to overcome it.

Weaknesses:

None.

Comments on revisions:

In response to the reviewers' questions and comments, the authors have revised the manuscript accordingly and sufficiently addressed the differences between their study and previous works on CDK4/6 and CDK2 combination therapy as a second-line approach.

Reviewer #2 (Public review):

Summary:

This study elucidated the mechanism underlying drug resistance induced by CDK4/6i as a single agent and proposed a novel and efficacious second-line therapeutic strategy. It highlighted the potential of combining CDK2i with CDK4/6i for the treatment of HR+/HER2- breast cancer.

Strengths:

The study demonstrated that CDK4/6 induces drug resistance by impairing Rb activation, which results in diminished E2F activity and a delay in G1 phase progression. It suggests that the synergistic use of CDK2i and CDK4/6i may represent a promising second-line treatment approach. Addressing critical clinical challenges, this study holds substantial practical implications.

Comments on revisions:

The author has comprehensively addressed all the questions I raised.

Reviewer #3 (Public review):

Summary:

In their manuscript, Armand and colleagues investigate the potential of continuing CDK4/6 inhibitors or combining them with CDK2 inhibitors in the treatment of breast cancer that has developed resistance to initial therapy. Utilizing cellular and animal models, the research examines whether maintaining CDK4/6 inhibition or adding CDK2 inhibitors can effectively control tumor growth after resistance has set in. The key findings from the study indicate that the sustained use of CDK4/6 inhibitors can slow down the proliferation of cancer cells that have become resistant, and the combination of CDK2 inhibitors with CDK4/6 inhibitors can further enhance the suppression of tumor growth. Additionally, the study identifies that high levels of Cyclin E play a significant role in resistance to the combined therapy. These results suggest that continuing CDK4/6 inhibitors along with the strategic use of CDK2 inhibitors could be an effective strategy to overcome treatment resistance in hormone receptor-positive breast cancer. However, several issues need to be addressed before considering its publication.

Strengths:

(1) Continuous CDK4/6 Inhibitor Treatment Significantly Suppresses the Growth of Drug-Resistant HR+ Breast Cancer: The study demonstrates that the continued use of CDK4/6 inhibitors, even after disease progression, can significantly inhibit the growth of drug-resistant breast cancer.

(2) Potential of Combined Use of CDK2 Inhibitors with CDK4/6 Inhibitors: The research highlights the potential of combining CDK2 inhibitors with CDK4/6 inhibitors to effectively suppress CDK2 activity and overcome drug resistance.

(3) Discovery of Cyclin E Overexpression as a Key Driver: The study identifies overexpression of cyclin E as a key driver of resistance to the combination of CDK4/6 and CDK2 inhibitors, providing insights for future cancer treatments.

(4) Consistency of In Vitro and In Vivo Experimental Results: The study obtained supportive results from both in vitro cell experiments and in vivo tumor models, enhancing the reliability of the research.

(5) Validation with Multiple Cell Lines: The research utilized multiple HR+/HER2- breast cancer cell lines (such as MCF-7, T47D, CAMA-1) and triple-negative breast cancer cell lines (such as MDA-MB-231), validating the broad applicability of the results.

Comments on revisions:

The authors made a significant effort to improve the manuscript. My comments were sufficiently addressed.